{"collection":"philosophy-ethics","full_text_available":true,"graph_url":"https://unchartedknowledge.5gfusion.net/v2/api/page/gutenberg_39713/graph","html_url":"https://unchartedknowledge.5gfusion.net/v2/page/gutenberg_39713","id":"gutenberg_39713","license":"Public Domain (US)","rights_basis":"gutenberg_metadata_copyright_false","source":"gutenberg","source_url":"https://www.gutenberg.org/ebooks/39713","summary":null,"tags":["Category: Mathematics","Category: Philosophy & Ethics","Category: Science - Physics","Mathematics -- Philosophy","Science -- Methodology","Science -- Philosophy"],"text":"Produced by Bryan Ness and the Online Distributed\nProofreading Team at http://www.pgdp.net (This book was\nproduced from scanned images of public domain material\nfrom the Google Print project.)\n\n\n\n\n\n\n\n\n\n SCIENCE AND EDUCATION\n\n A SERIES OF VOLUMES FOR THE PROMOTION OF\n SCIENTIFIC RESEARCH AND EDUCATIONAL PROGRESS\n\n EDITED BY J. MCKEEN CATTELL\n\n\n VOLUME I--THE FOUNDATIONS OF SCIENCE\n\n\n\n\n UNDER THE SAME EDITORSHIP\n\n\n SCIENCE AND EDUCATION. A series of volumes for the promotion of\n scientific research and educational progress.\n\n Volume I. The Foundations of Science. By H. POINCAR\u00c9. Containing\n the authorised English translation by George Bruce Halsted of\n \"Science and Hypothesis,\" \"The Value of Science,\" and \"Science\n and Method.\"\n\n Volume II. Medical Research and Education. By Richard Mills\n Pearce, William H. Welch, W. H. Howell, Franklin P. Mall,\n Lewellys F. Barker, Charles S. Minot, W. B. Cannon, W. T.\n Councilman Theobald Smith, G. N. Stewart, C. M. Jackson,\n E. P. Lyon, James B. Herrick, John M. Dodson, C. R. Bardeen,\n W. Ophuls, S. J. Meltzer, James Ewing, W. W. Keen, Henry H.\n Donaldson, Christian A. Herter, and Henry P. Bowditch.\n\n Volume III. University Control. By J. MCKEEN CATTELL and other\n authors.\n\n AMERICAN MEN OF SCIENCE. A Biographical Directory.\n\n SCIENCE. A weekly journal devoted to the advancement of science.\n The official organ of the American Association for the\n Advancement of Science.\n\n THE POPULAR SCIENCE MONTHLY. A monthly magazine devoted to the\n diffusion of science.\n\n THE AMERICAN NATURALIST. A monthly journal devoted to the\n biological sciences, with special reference to the factors\n of evolution.\n\n THE SCIENCE PRESS\n\n NEW YORK GARRISON, N. Y.\n\n\n\n\n THE FOUNDATIONS\n OF SCIENCE\n\n SCIENCE AND HYPOTHESIS\n THE VALUE OF SCIENCE\n SCIENCE AND METHOD\n\n\n BY\n H. POINCAR\u00c9\n\n\n AUTHORIZED TRANSLATION BY\n GEORGE BRUCE HALSTED\n\n\n WITH A SPECIAL PREFACE BY POINCAR\u00c9, AND AN INTRODUCTION\n BY JOSIAH ROYCE, HARVARD UNIVERSITY\n\n\n THE SCIENCE PRESS\n NEW YORK AND GARRISON, N. Y.\n 1913\n\n\n\n\n Copyright, 1913\n BY THE SCIENCE PRESS\n\n\n PRESS OF\n THE NEW ERA PRINTING COMPANY\n LANCASTER, PA.\n\n\n\n\nCONTENTS\n\n\n PAGE\n Henri Poincar\u00e9 ix\n Author's Preface to the Translation 3\n\n\nSCIENCE AND HYPOTHESIS\n\n Introduction by Royce 9\n Introduction 27\n\n PART I. _Number and Magnitude_\n\n CHAPTER I.--On the Nature of Mathematical Reasoning 31\n Syllogistic Deduction 31\n Verification and Proof 32\n Elements of Arithmetic 33\n Reasoning by Recurrence 37\n Induction 40\n Mathematical Construction 41\n\n CHAPTER II.--Mathematical Magnitude and Experience 43\n Definition of Incommensurables 44\n The Physical Continuum 46\n Creation of the Mathematical Continuum 46\n Measurable Magnitude 49\n Various Remarks (Curves without Tangents) 50\n The Physical Continuum of Several Dimensions 52\n The Mathematical Continuum of Several Dimensions 53\n\n PART II. _Space_\n\n CHAPTER III.--The Non-Euclidean Geometries 55\n The Bolyai-Lobachevski Geometry 56\n Riemann's Geometry 57\n The Surfaces of Constant Curvature 58\n Interpretation of Non-Euclidean Geometries 59\n The Implicit Axioms 60\n The Fourth Geometry 62\n Lie's Theorem 62\n Riemann's Geometries 63\n On the Nature of Axioms 63\n\n CHAPTER IV.--Space and Geometry 66\n Geometric Space and Perceptual Space 66\n Visual Space 67\n Tactile Space and Motor Space 68\n Characteristics of Perceptual Space 69\n Change of State and Change of Position 70\n Conditions of Compensation 72\n Solid Bodies and Geometry 72\n Law of Homogeneity 74\n The Non-Euclidean World 75\n The World of Four Dimensions 78\n Conclusions 79\n\n CHAPTER V.--Experience and Geometry 81\n Geometry and Astronomy 81\n The Law of Relativity 83\n Bearing of Experiments 86\n Supplement (What is a Point?) 89\n Ancestral Experience 91\n\n PART III. _Force_\n\n CHAPTER VI.--The Classic Mechanics 92\n The Principle of Inertia 93\n The Law of Acceleration 97\n Anthropomorphic Mechanics 103\n The School of the Thread 104\n\n CHAPTER VII.--Relative Motion and Absolute Motion 107\n The Principle of Relative Motion 107\n Newton's Argument 108\n\n CHAPTER VIII.--Energy and Thermodynamics 115\n Energetics 115\n Thermodynamics 119\n General Conclusions on Part III 123\n\n PART IV. _Nature_\n\n CHAPTER IX.--Hypotheses in Physics 127\n The R\u00f4le of Experiment and Generalization 127\n The Unity of Nature 130\n The R\u00f4le of Hypothesis 133\n Origin of Mathematical Physics 136\n\n CHAPTER X.--The Theories of Modern Physics 140\n Meaning of Physical Theories 140\n Physics and Mechanism 144\n Present State of the Science 148\n\n CHAPTER XI.--The Calculus of Probabilities 155\n Classification of the Problems of Probability 158\n Probability in Mathematics 161\n Probability in the Physical Sciences 164\n Rouge et noir 167\n The Probability of Causes 169\n The Theory of Errors 170\n Conclusions 172\n\n CHAPTER XII.--Optics and Electricity 174\n Fresnel's Theory 174\n Maxwell's Theory 175\n The Mechanical Explanation of Physical Phenomena 177\n\n CHAPTER XIII.--Electrodynamics 184\n Amp\u00e8re's Theory 184\n Closed Currents 185\n Action of a Closed Current on a Portion of Current 186\n Continuous Rotations 187\n Mutual Action of Two Open Currents 189\n Induction 190\n Theory of Helmholtz 191\n Difficulties Raised by these Theories 193\n Maxwell's Theory 193\n Rowland's Experiment 194\n The Theory of Lorentz 196\n\n\nTHE VALUE OF SCIENCE\n\n Translator's Introduction 201\n Does the Scientist Create Science? 201\n The Mind Dispelling Optical Illusions 202\n Euclid not Necessary 202\n Without Hypotheses, no Science 203\n What Outcome? 203\n Introduction 205\n\n PART I. _The Mathematical Sciences_\n\n CHAPTER I.--Intuition and Logic in Mathematics 210\n\n CHAPTER II.--The Measure of Time 223\n\n CHAPTER III.--The Notion of Space 235\n Qualitative Geometry 238\n The Physical Continuum of Several Dimensions 240\n The Notion of Point 244\n The Notion of Displacement 247\n Visual Space 252\n\n CHAPTER IV.--Space and its Three Dimensions 256\n The Group of Displacements 256\n Identity of Two Points 259\n Tactile Space 264\n Identity of the Different Spaces 268\n Space and Empiricism 271\n R\u00f4le of the Semicircular Canals 276\n\n PART II. _The Physical Sciences_\n\n CHAPTER V.--Analysis and Physics 279\n\n CHAPTER VI.--Astronomy 289\n\n CHAPTER VII.--The History of Mathematical Physics 297\n The Physics of Central Forces 297\n The Physics of the Principles 299\n\n CHAPTER VIII.--The Present Crisis in Physics 303\n The New Crisis 303\n Carnot's Principle 303\n The Principle of Relativity 305\n Newton's Principle 308\n Lavoisier's Principle 310\n Mayer's Principle 312\n\n CHAPTER IX.--The Future of Mathematical Physics 314\n The Principles and Experiment 314\n The R\u00f4le of the Analyst 314\n Aberration and Astronomy 315\n Electrons and Spectra 316\n Conventions preceding Experiment 317\n Future Mathematical Physics 319\n\n PART III. _The Objective Value of Science_\n\n CHAPTER X.--Is Science Artificial? 321\n The Philosophy of LeRoy 321\n Science, Rule of Action 323\n The Crude Fact and the Scientific Fact 325\n Nominalism and the Universal Invariant 333\n\n CHAPTER XI.--Science and Reality 340\n Contingence and Determinism 340\n Objectivity of Science 347\n The Rotation of the Earth 353\n Science for Its Own Sake 354\n\n\nSCIENCE AND METHOD\n\n Introduction 359\n\n BOOK I. _Science and the Scientist_\n\n CHAPTER I.--The Choice of Facts 362\n\n CHAPTER II.--The Future of Mathematics 369\n\n CHAPTER III.--Mathematical Creation 383\n\n CHAPTER IV.--Chance 395\n\n BOOK II. _Mathematical Reasoning_\n\n CHAPTER I.--The Relativity of Space 413\n\n CHAPTER II.--Mathematical Definitions and Teaching 430\n\n CHAPTER III.--Mathematics and Logic 448\n\n CHAPTER IV.--The New Logics 460\n\n CHAPTER V.--The Latest Efforts of the Logisticians 472\n\n BOOK III. _The New Mechanics_\n\n CHAPTER I.--Mechanics and Radium 486\n\n CHAPTER II.--Mechanics and Optics 496\n\n CHAPTER III.--The New Mechanics and Astronomy 512\n\n BOOK IV. _Astronomic Science_\n\n CHAPTER I.--The Milky Way and the Theory of Gases 523\n\n CHAPTER II.--French Geodesy 535\n\n General Conclusions 544\n\n Index 547\n\n\n\n\nHENRI POINCAR\u00c9\n\n\nSIR GEORGE DARWIN, worthy son of an immortal father, said, referring to\nwhat Poincar\u00e9 was to him and to his work: \"He must be regarded as the\npresiding genius--or, shall I say, my patron saint?\"\n\nHenri Poincar\u00e9 was born April 29, 1854, at Nancy, where his father was a\nphysician highly respected. His schooling was broken into by the war of\n1870-71, to get news of which he learned to read the German newspapers.\nHe outclassed the other boys of his age in all subjects and in 1873\npassed highest into the \u00c9cole Polytechnique, where, like John Bolyai at\nMaros V\u00e1s\u00e1rhely, he followed the courses in mathematics without taking a\nnote and without the syllabus. He proceeded in 1875 to the School of\nMines, and was _Nomm\u00e9_, March 26, 1879. But he won his doctorate in the\nUniversity of Paris, August 1, 1879, and was appointed to teach in the\nFacult\u00e9 des Sciences de Caen, December 1, 1879, whence he was quickly\ncalled to the University of Paris, teaching there from October 21, 1881,\nuntil his death, July 17, 1912. So it is an error to say he started as\nan engineer. At the early age of thirty-two he became a member of\nl'Acad\u00e9mie des Sciences, and, March 5, 1908, was chosen Membre de\nl'Acad\u00e9mie Fran\u00e7aise. July 1, 1909, the number of his writings was 436.\n\nHis earliest publication was in 1878, and was not important. Afterward\ncame an essay submitted in competition for the Grand Prix offered in\n1880, but it did not win. Suddenly there came a change, a striking fire,\na bursting forth, in February, 1881, and Poincar\u00e9 tells us the very\nminute it happened. Mounting an omnibus, \"at the moment when I put my\nfoot upon the step, the idea came to me, without anything in my previous\nthoughts seeming to foreshadow it, that the transformations I had used\nto define the Fuchsian functions were identical with those of\nnon-Euclidean geometry.\" Thereby was opened a perspective new and\nimmense. Moreover, the magic wand of his whole life-work had been\ngrasped, the Aladdin's lamp had been rubbed, non-Euclidean geometry,\nwhose necromancy was to open up a new theory of our universe, whose\nbrilliant exposition was commenced in his book _Science and Hypothesis_,\nwhich has been translated into six languages and has already had a\ncirculation of over 20,000. The non-Euclidean notion is that of the\npossibility of alternative laws of nature, which in the Introduction to\nthe _\u00c9lectricit\u00e9 et Optique_, 1901, is thus put: \"If therefore a\nphenomenon admits of a complete mechanical explanation, it will admit of\nan infinity of Others which will account equally well for all the\npeculiarities disclosed by experiment.\"\n\nThe scheme of laws of nature so largely due to Newton is merely one of\nan infinite number of conceivable rational schemes for helping us master\nand make experience; it is _commode_, convenient; but perhaps another\nmay be vastly more advantageous. The old conception of _true_ has been\nrevised. The first expression of the new idea occurs on the title page\nof John Bolyai's marvelous _Science Absolute of Space_, in the phrase\n\"haud unquam a priori decidenda.\"\n\nWith bearing on the history of the earth and moon system and the origin\nof double stars, in formulating the geometric criterion of stability,\nPoincar\u00e9 proved the existence of a previously unknown pear-shaped\nfigure, with the possibility that the progressive deformation of this\nfigure with increasing angular velocity might result in the breaking up\nof the rotating body into two detached masses. Of his treatise _Les\nM\u00e9thodes nouvelles de la M\u00e9chanique c\u00e9leste_, Sir George Darwin says:\n\"It is probable that for half a century to come it will be the mine from\nwhich humbler investigators will excavate their materials.\" Brilliant\nwas his appreciation of Poincar\u00e9 in presenting the gold medal of the\nRoyal Astronomical Society. The three others most akin in genius are\nlinked with him by the Sylvester medal of the Royal Society, the\nLobachevski medal of the Physico-Mathematical Society of Kazan, and the\nBolyai prize of the Hungarian Academy of Sciences. His work must be\nreckoned with the greatest mathematical achievements of mankind.\n\nThe kernel of Poincar\u00e9's power lies in an oracle Sylvester often quoted\nto me as from Hesiod: The whole is less than its part.\n\nHe penetrates at once the divine simplicity of the perfectly general\ncase, and thence descends, as from Olympus, to the special concrete\nearthly particulars.\n\nA combination of seemingly extremely simple analytic and geometric\nconcepts gave necessary general conclusions of immense scope from which\nsprang a disconcerting wilderness of possible deductions. And so he\nleaves a noble, fruitful heritage.\n\nSays Love: \"His right is recognized now, and it is not likely that\nfuture generations will revise the judgment, to rank among the greatest\nmathematicians of all time.\"\n\n GEORGE BRUCE HALSTED.\n\n\n * * * * *\n\n\n\n\nSCIENCE AND HYPOTHESIS\n\n\n\n\n * * * * *\n\n\n\n\nAUTHOR'S PREFACE TO THE TRANSLATION\n\n\nI am exceedingly grateful to Dr. Halsted, who has been so good as to\npresent my book to American readers in a translation, clear and\nfaithful.\n\nEvery one knows that this savant has already taken the trouble to\ntranslate many European treatises and thus has powerfully contributed to\nmake the new continent understand the thought of the old.\n\nSome people love to repeat that Anglo-Saxons have not the same way of\nthinking as the Latins or as the Germans; that they have quite another\nway of understanding mathematics or of understanding physics; that this\nway seems to them superior to all others; that they feel no need of\nchanging it, nor even of knowing the ways of other peoples.\n\nIn that they would beyond question be wrong, but I do not believe that\nis true, or, at least, that is true no longer. For some time the English\nand Americans have been devoting themselves much more than formerly to\nthe better understanding of what is thought and said on the continent of\nEurope.\n\nTo be sure, each people will preserve its characteristic genius, and it\nwould be a pity if it were otherwise, supposing such a thing possible.\nIf the Anglo-Saxons wished to become Latins, they would never be more\nthan bad Latins; just as the French, in seeking to imitate them, could\nturn out only pretty poor Anglo-Saxons.\n\nAnd then the English and Americans have made scientific conquests they\nalone could have made; they will make still more of which others would\nbe incapable. It would therefore be deplorable if there were no longer\nAnglo-Saxons.\n\nBut continentals have on their part done things an Englishman could not\nhave done, so that there is no need either for wishing all the world\nAnglo-Saxon.\n\nEach has his characteristic aptitudes, and these aptitudes should be\ndiverse, else would the scientific concert resemble a quartet where\nevery one wanted to play the violin.\n\nAnd yet it is not bad for the violin to know what the violon-cello is\nplaying, and _vice versa_.\n\nThis it is that the English and Americans are comprehending more and\nmore; and from this point of view the translations undertaken by Dr.\nHalsted are most opportune and timely.\n\nConsider first what concerns the mathematical sciences. It is frequently\nsaid the English cultivate them only in view of their applications and\neven that they despise those who have other aims; that speculations too\nabstract repel them as savoring of metaphysic.\n\nThe English, even in mathematics, are to proceed always from the\nparticular to the general, so that they would never have an idea of\nentering mathematics, as do many Germans, by the gate of the theory of\naggregates. They are always to hold, so to speak, one foot in the world\nof the senses, and never burn the bridges keeping them in communication\nwith reality. They thus are to be incapable of comprehending or at least\nof appreciating certain theories more interesting than utilitarian, such\nas the non-Euclidean geometries. According to that, the first two parts\nof this book, on number and space, should seem to them void of all\nsubstance and would only baffle them.\n\nBut that is not true. And first of all, are they such uncompromising\nrealists as has been said? Are they absolutely refractory, I do not say\nto metaphysic, but at least to everything metaphysical?\n\nRecall the name of Berkeley, born in Ireland doubtless, but immediately\nadopted by the English, who marked a natural and necessary stage in the\ndevelopment of English philosophy.\n\nIs this not enough to show they are capable of making ascensions\notherwise than in a captive balloon?\n\nAnd to return to America, is not the _Monist_ published at Chicago, that\nreview which even to us seems bold and yet which finds readers?\n\nAnd in mathematics? Do you think American geometers are concerned only\nabout applications? Far from it. The part of the science they cultivate\nmost devotedly is the theory of groups of substitutions, and under its\nmost abstract form, the farthest removed from the practical.\n\nMoreover, Dr. Halsted gives regularly each year a review of all\nproductions relative to the non-Euclidean geometry, and he has about him\na public deeply interested in his work. He has initiated this public\ninto the ideas of Hilbert, and he has even written an elementary\ntreatise on 'Rational Geometry,' based on the principles of the renowned\nGerman savant.\n\nTo introduce this principle into teaching is surely this time to burn\nall bridges of reliance upon sensory intuition, and this is, I confess,\na boldness which seems to me almost rashness.\n\nThe American public is therefore much better prepared than has been\nthought for investigating the origin of the notion of space.\n\nMoreover, to analyze this concept is not to sacrifice reality to I know\nnot what phantom. The geometric language is after all only a language.\nSpace is only a word that we have believed a thing. What is the origin\nof this word and of other words also? What things do they hide? To ask\nthis is permissible; to forbid it would be, on the contrary, to be a\ndupe of words; it would be to adore a metaphysical idol, like savage\npeoples who prostrate themselves before a statue of wood without daring\nto take a look at what is within.\n\nIn the study of nature, the contrast between the Anglo-Saxon spirit and\nthe Latin spirit is still greater.\n\nThe Latins seek in general to put their thought in mathematical form;\nthe English prefer to express it by a material representation.\n\nBoth doubtless rely only on experience for knowing the world; when they\nhappen to go beyond this, they consider their foreknowledge as only\nprovisional, and they hasten to ask its definitive confirmation from\nnature herself.\n\nBut experience is not all, and the savant is not passive; he does not\nwait for the truth to come and find him, or for a chance meeting to\nbring him face to face with it. He must go to meet it, and it is for his\nthinking to reveal to him the way leading thither. For that there is\nneed of an instrument; well, just there begins the difference--the\ninstrument the Latins ordinarily choose is not that preferred by the\nAnglo-Saxons.\n\nFor a Latin, truth can be expressed only by equations; it must obey laws\nsimple, logical, symmetric and fitted to satisfy minds in love with\nmathematical elegance.\n\nThe Anglo-Saxon to depict a phenomenon will first be engrossed in making\na _model_, and he will make it with common materials, such as our crude,\nunaided senses show us them. He also makes a hypothesis, he assumes\nimplicitly that nature, in her finest elements, is the same as in the\ncomplicated aggregates which alone are within the reach of our senses.\nHe concludes from the body to the atom.\n\nBoth therefore make hypotheses, and this indeed is necessary, since no\nscientist has ever been able to get on without them. The essential thing\nis never to make them unconsciously.\n\nFrom this point of view again, it would be well for these two sorts of\nphysicists to know something of each other; in studying the work of\nminds so unlike their own, they will immediately recognize that in this\nwork there has been an accumulation of hypotheses.\n\nDoubtless this will not suffice to make them comprehend that they on\ntheir part have made just as many; each sees the mote without seeing the\nbeam; but by their criticisms they will warn their rivals, and it may be\nsupposed these will not fail to render them the same service.\n\nThe English procedure often seems to us crude, the analogies they think\nthey discover to us seem at times superficial; they are not sufficiently\ninterlocked, not precise enough; they sometimes permit incoherences,\ncontradictions in terms, which shock a geometric spirit and which the\nemployment of the mathematical method would immediately have put in\nevidence. But most often it is, on the other hand, very fortunate that\nthey have not perceived these contradictions; else would they have\nrejected their model and could not have deduced from it the brilliant\nresults they have often made to come out of it.\n\nAnd then these very contradictions, when they end by perceiving them,\nhave the advantage of showing them the hypothetical character of their\nconceptions, whereas the mathematical method, by its apparent rigor and\ninflexible course, often inspires in us a confidence nothing warrants,\nand prevents our looking about us.\n\nFrom another point of view, however, the two conceptions are very\nunlike, and if all must be said, they are very unlike because of a\ncommon fault.\n\nThe English wish to make the world out of what we see. I mean what we\nsee with the unaided eye, not the microscope, nor that still more\nsubtile microscope, the human head guided by scientific induction.\n\nThe Latin wants to make it out of formulas, but these formulas are still\nthe quintessenced expression of what we see. In a word, both would make\nthe unknown out of the known, and their excuse is that there is no way\nof doing otherwise.\n\nAnd yet is this legitimate, if the unknown be the simple and the known\nthe complex?\n\nShall we not get of the simple a false idea, if we think it like the\ncomplex, or worse yet if we strive to make it out of elements which are\nthemselves compounds?\n\nIs not each great advance accomplished precisely the day some one has\ndiscovered under the complex aggregate shown by our senses something far\nmore simple, not even resembling it--as when Newton replaced Kepler's\nthree laws by the single law of gravitation, which was something\nsimpler, equivalent, yet unlike?\n\nOne is justified in asking if we are not on the eve of just such a\nrevolution or one even more important. Matter seems on the point of\nlosing its mass, its solidest attribute, and resolving itself into\nelectrons. Mechanics must then give place to a broader conception which\nwill explain it, but which it will not explain.\n\nSo it was in vain the attempt was made in England to construct the ether\nby material models, or in France to apply to it the laws of dynamic.\n\nThe ether it is, the unknown, which explains matter, the known; matter\nis incapable of explaining the ether.\n\n POINCAR\u00c9.\n\n\n\n\nINTRODUCTION\n\nBY PROFESSOR JOSIAH ROYCE\n\nHARVARD UNIVERSITY\n\n\nThe treatise of a master needs no commendation through the words of a\nmere learner. But, since my friend and former fellow student, the\ntranslator of this volume, has joined with another of my colleagues,\nProfessor Cattell, in asking me to undertake the task of calling the\nattention of my fellow students to the importance and to the scope of M.\nPoincar\u00e9's volume, I accept the office, not as one competent to pass\njudgment upon the book, but simply as a learner, desirous to increase\nthe number of those amongst us who are already interested in the type of\nresearches to which M. Poincar\u00e9 has so notably contributed.\n\n\nI\n\nThe branches of inquiry collectively known as the Philosophy of Science\nhave undergone great changes since the appearance of Herbert Spencer's\n_First Principles_, that volume which a large part of the general public\nin this country used to regard as the representative compend of all\nmodern wisdom relating to the foundations of scientific knowledge. The\nsummary which M. Poincar\u00e9 gives, at the outset of his own introduction\nto the present work, where he states the view which the 'superficial\nobserver' takes of scientific truth, suggests, not indeed Spencer's own\nmost characteristic theories, but something of the spirit in which many\ndisciples of Spencer interpreting their master's formulas used to\nconceive the position which science occupies in dealing with experience.\nIt was well known to them, indeed, that experience is a constant guide,\nand an inexhaustible source both of novel scientific results and of\nunsolved problems; but the fundamental Spencerian principles of science,\nsuch as 'the persistence of force,' the 'rhythm of motion' and the rest,\nwere treated by Spencer himself as demonstrably objective, although\nindeed 'relative' truths, capable of being tested once for all by the\n'inconceivability of the opposite,' and certain to hold true for the\nwhole 'knowable' universe. Thus, whether one dwelt upon the results of\nsuch a mathematical procedure as that to which M. Poincar\u00e9 refers in his\nopening paragraphs, or whether, like Spencer himself, one applied the\n'first principles' to regions of less exact science, this confidence\nthat a certain orthodoxy regarding the principles of science was\nestablished forever was characteristic of the followers of the movement\nin question. Experience, lighted up by reason, seemed to them to have\npredetermined for all future time certain great theoretical results\nregarding the real constitution of the 'knowable' cosmos. Whoever\ndoubted this doubted 'the verdict of science.'\n\nSome of us well remember how, when Stallo's 'Principles and Theories of\nModern Physics' first appeared, this sense of scientific orthodoxy was\nshocked amongst many of our American readers and teachers of science. I\nmyself can recall to mind some highly authoritative reviews of that work\nin which the author was more or less sharply taken to task for his\nignorant presumption in speaking with the freedom that he there used\nregarding such sacred possessions of humanity as the fundamental\nconcepts of physics. That very book, however, has quite lately been\ntranslated into German as a valuable contribution to some of the most\nrecent efforts to reconstitute a modern 'philosophy of nature.' And\nwhatever may be otherwise thought of Stallo's critical methods, or of\nhis results, there can be no doubt that, at the present moment, if his\nbook were to appear for the first time, nobody would attempt to\ndiscredit the work merely on account of its disposition to be agnostic\nregarding the objective reality of the concepts of the kinetic theory of\ngases, or on account of its call for a logical rearrangement of the\nfundamental concepts of the theory of energy. We are no longer able so\neasily to know heretics at first sight.\n\nFor we now appear to stand in this position: The control of natural\nphenomena, which through the sciences men have attained, grows daily\nvaster and more detailed, and in its details more assured. Phenomena men\nknow and predict better than ever. But regarding the most general\ntheories, and the most fundamental, of science, there is no longer any\nnotable scientific orthodoxy. Thus, as knowledge grows firmer and wider,\nconceptual construction becomes less rigid. The field of the theoretical\nphilosophy of nature--yes, the field of the logic of science--this whole\nregion is to-day an open one. Whoever will work there must indeed accept\nthe verdict of experience regarding what happens in the natural world.\nSo far he is indeed bound. But he may undertake without hindrance from\nmere tradition the task of trying afresh to reduce what happens to\nconceptual unity. The circle-squarers and the inventors of devices for\nperpetual motion are indeed still as unwelcome in scientific company as\nthey were in the days when scientific orthodoxy was more rigidly\ndefined; but that is not because the foundations of geometry are now\nviewed as completely settled, beyond controversy, nor yet because the\n'persistence of force' has been finally so defined as to make the\n'opposite inconceivable' and the doctrine of energy beyond the reach of\nnovel formulations. No, the circle-squarers and the inventors of devices\nfor perpetual motion are to-day discredited, not because of any\nunorthodoxy of their general philosophy of nature, but because their\nviews regarding special facts and processes stand in conflict with\ncertain equally special results of science which themselves admit of\nvery various general theoretical interpretations. Certain properties of\nthe irrational number [pi] are known, in sufficient multitude to justify\nthe mathematician in declining to listen to the arguments of the\ncircle-squarer; but, despite great advances, and despite the assured\nresults of Dedekind, of Cantor, of Weierstrass and of various others,\nthe general theory of the logic of the numbers, rational and irrational,\nstill presents several important features of great obscurity; and the\nphilosophy of the concepts of geometry yet remains, in several very\nnotable respects, unconquered territory, despite the work of Hilbert and\nof Pieri, and of our author himself. The ordinary inventors of the\nperpetual motion machines still stand in conflict with accepted\ngeneralizations; but nobody knows as yet what the final form of the\ntheory of energy will be, nor can any one say precisely what place the\nphenomena of the radioactive bodies will occupy in that theory. The\nalchemists would not be welcome workers in modern laboratories; yet\nsome sorts of transformation and of evolution of the elements are to-day\nmatters which theory can find it convenient, upon occasion, to treat as\nmore or less exactly definable possibilities; while some newly observed\nphenomena tend to indicate, not indeed that the ancient hopes of the\nalchemists were well founded, but that the ultimate constitution of\nmatter is something more fluent, less invariant, than the theoretical\northodoxy of a recent period supposed. Again, regarding the foundations\nof biology, a theoretical orthodoxy grows less possible, less definable,\nless conceivable (even as a hope) the more knowledge advances. Once\n'mechanism' and 'vitalism' were mutually contradictory theories\nregarding the ultimate constitution of living bodies. Now they are\nobviously becoming more and more 'points of view,' diverse but not\nnecessarily conflicting. So far as you find it convenient to limit your\nstudy of vital processes to those phenomena which distinguish living\nmatter from all other natural objects, you may assume, in the modern\n'pragmatic' sense, the attitude of a 'neo-vitalist.' So far, however, as\nyou are able to lay stress, with good results, upon the many ways in\nwhich the life processes can be assimilated to those studied in physics\nand in chemistry, you work as if you were a partisan of 'mechanics.' In\nany case, your special science prospers by reason of the empirical\ndiscoveries that you make. And your theories, whatever they are, must\nnot run counter to any positive empirical results. But otherwise,\nscientific orthodoxy no longer predetermines what alone it is\nrespectable for you to think about the nature of living substance.\n\nThis gain in the freedom of theory, coming, as it does, side by side\nwith a constant increase of a positive knowledge of nature, lends itself\nto various interpretations, and raises various obvious questions.\n\n\nII\n\nOne of the most natural of these interpretations, one of the most\nobvious of these questions, may be readily stated. Is not the lesson of\nall these recent discussions simply this, that general theories are\nsimply vain, that a philosophy of nature is an idle dream, and that the\nresults of science are coextensive with the range of actual empirical\nobservation and of successful prediction? If this is indeed the lesson,\nthen the decline of theoretical orthodoxy in science is--like the\neclipse of dogma in religion--merely a further lesson in pure\npositivism, another proof that man does best when he limits himself to\nthinking about what can be found in human experience, and in trying to\nplan what can be done to make human life more controllable and more\nreasonable. What we are free to do as we please--is it any longer a\nserious business? What we are free to think as we please--is it of any\nfurther interest to one who is in search of truth? If certain general\ntheories are mere conceptual constructions, which to-day are, and\nto-morrow are cast into the oven, why dignify them by the name of\nphilosophy? Has science any place for such theories? Why be a\n'neo-vitalist,' or an 'evolutionist,' or an 'atomist,' or an\n'Energetiker'? Why not say, plainly: \"Such and such phenomena, thus and\nthus described, have been observed; such and such experiences are to be\nexpected, since the hypotheses by the terms of which we are required to\nexpect them have been verified too often to let us regard the agreement\nwith experience as due merely to chance; so much then with reasonable\nassurance we know; all else is silence--or else is some matter to be\ntested by another experiment?\" Why not limit our philosophy of science\nstrictly to such a counsel of resignation? Why not substitute, for the\nold scientific orthodoxy, simply a confession of ignorance, and a\nresolution to devote ourselves to the business of enlarging the bounds\nof actual empirical knowledge?\n\nSuch comments upon the situation just characterized are frequently made.\nUnfortunately, they seem not to content the very age whose revolt from\nthe orthodoxy of traditional theory, whose uncertainty about all\ntheoretical formulations, and whose vast wealth of empirical discoveries\nand of rapidly advancing special researches, would seem most to justify\nthese very comments. Never has there been better reason than there is\nto-day to be content, if rational man could be content, with a pure\npositivism. The splendid triumphs of special research in the most\nvarious fields, the constant increase in our practical control over\nnature--these, our positive and growing possessions, stand in glaring\ncontrast to the failure of the scientific orthodoxy of a former period\nto fix the outlines of an ultimate creed about the nature of the\nknowable universe. Why not 'take the cash and let the credit go'? Why\npursue the elusive theoretical 'unification' any further, when what we\ndaily get from our sciences is an increasing wealth of detailed\ninformation and of practical guidance?\n\nAs a fact, however, the known answer of our own age to these very\nobvious comments is a constant multiplication of new efforts towards\nlarge and unifying theories. If theoretical orthodoxy is no longer\nclearly definable, theoretical construction was never more rife. The\nhistory of the doctrine of evolution, even in its most recent phases,\nwhen the theoretical uncertainties regarding the 'factors of evolution'\nare most insisted upon, is full of illustrations of this remarkable\nunion of scepticism in critical work with courage regarding the use of\nthe scientific imagination. The history of those controversies regarding\ntheoretical physics, some of whose principal phases M. Poincar\u00e9, in his\nbook, sketches with the hand of the master, is another illustration of\nthe consciousness of the time. Men have their freedom of thought in\nthese regions; and they feel the need of making constant and\nconstructive use of this freedom. And the men who most feel this need\nare by no means in the majority of cases professional metaphysicians--or\nstudents who, like myself, have to view all these controversies amongst\nthe scientific theoreticians from without as learners. These large\ntheoretical constructions are due, on the contrary, in a great many\ncases to special workers, who have been driven to the freedom of\nphilosophy by the oppression of experience, and who have learned in the\nconflict with special problems the lesson that they now teach in the\nform of general ideas regarding the philosophical aspects of science.\n\nWhy, then, does science actually need general theories, despite the fact\nthat these theories inevitably alter and pass away? What is the service\nof a philosophy of science, when it is certain that the philosophy of\nscience which is best suited to the needs of one generation must be\nsuperseded by the advancing insight of the next generation? Why must\nthat which endlessly grows, namely, man's knowledge of the phenomenal\norder of nature, be constantly united in men's minds with that which is\ncertain to decay, namely, the theoretical formulation of special\nknowledge in more or less completely unified systems of doctrine?\n\nI understand our author's volume to be in the main an answer to this\nquestion. To be sure, the compact and manifold teachings which this text\ncontains relate to a great many different special issues. A student\ninterested in the problems of the philosophy of mathematics, or in the\ntheory of probabilities, or in the nature and office of mathematical\nphysics, or in still other problems belonging to the wide field here\ndiscussed, may find what he wants here and there in the text, even in\ncase the general issues which give the volume its unity mean little to\nhim, or even if he differs from the author's views regarding the\nprincipal issues of the book. But in the main, this volume must be\nregarded as what its title indicates--a critique of the nature and place\nof hypothesis in the work of science and a study of the logical\nrelations of theory and fact. The result of the book is a substantial\njustification of the scientific utility of theoretical construction--an\nabandonment of dogma, but a vindication of the rights of the\nconstructive reason.\n\n\nIII\n\nThe most notable of the results of our author's investigation of the\nlogic of scientific theories relates, as I understand his work, to a\ntopic which the present state of logical investigation, just summarized,\nmakes especially important, but which has thus far been very\ninadequately treated in the text-books of inductive logic. The useful\nhypotheses of science are of two kinds:\n\n1. The hypotheses which are valuable _precisely_ because they are either\nverifiable or else refutable through a definite appeal to the tests\nfurnished by experience; and\n\n2. The hypotheses which, despite the fact that experience suggests them,\nare valuable _despite_, or even _because_, of the fact that experience\ncan _neither_ confirm nor refute them. The contrast between these two\nkinds of hypotheses is a prominent topic of our author's discussion.\n\nHypotheses of the general type which I have here placed first in order\nare the ones which the text-books of inductive logic and those summaries\nof scientific method which are customary in the course of the elementary\ntreatises upon physical science are already accustomed to recognize and\nto characterize. The value of such hypotheses is indeed undoubted. But\nhypotheses of the type which I have here named in the second place are\nfar less frequently recognized in a perfectly explicit way as useful\naids in the work of special science. One usually either fails to admit\ntheir presence in scientific work, or else remains silent as to the\nreasons of their usefulness. Our author's treatment of the work of\nscience is therefore especially marked by the fact that he explicitly\nmakes prominent both the existence and the scientific importance of\nhypotheses of this second type. They occupy in his discussion a place\nsomewhat analogous to each of the two distinct positions occupied by the\n'categories' and the 'forms of sensibility,' on the one hand, and by the\n'regulative principles of the reason,' on the other hand, in the Kantian\ntheory of our knowledge of nature. That is, these hypotheses which can\nneither be confirmed nor refuted by experience appear, in M. Poincar\u00e9's\naccount, partly (like the conception of 'continuous quantity') as\ndevices of the understanding whereby we give conceptual unity and an\ninvisible connectedness to certain types of phenomenal facts which come\nto us in a discrete form and in a confused variety; and partly (like the\nlarger organizing concepts of science) as principles regarding the\nstructure of the world in its wholeness; _i. e._, as principles in the\nlight of which we try to interpret our experience, so as to give to it a\ntotality and an inclusive unity such as Euclidean space, or such as the\nworld of the theory of energy is conceived to possess. Thus viewed, M.\nPoincar\u00e9's logical theory of this second class of hypotheses undertakes\nto accomplish, with modern means and in the light of to-day's issues, a\npart of what Kant endeavored to accomplish in his theory of scientific\nknowledge with the limited means which were at his disposal. Those\naspects of science which are determined by the use of the hypotheses of\nthis second kind appear in our author's account as constituting an\nessential human way of viewing nature, an interpretation rather than a\nportrayal or a prediction of the objective facts of nature, an\nadjustment of our conceptions of things to the internal needs of our\nintelligence, rather than a grasping of things as they are in\nthemselves.\n\nTo be sure, M. Poincar\u00e9's view, in this portion of his work, obviously\ndiffers, meanwhile, from that of Kant, as well as this agrees, in a\nmeasure, with the spirit of the Kantian epistemology. I do not mean\ntherefore to class our author as a Kantian. For Kant, the\ninterpretations imposed by the 'forms of sensibility,' and by the\n'categories of the understanding,' upon our doctrine of nature are\nrigidly predetermined by the unalterable 'form' of our intellectual\npowers. We 'must' thus view facts, whatever the data of sense must be.\nThis, of course, is not M. Poincar\u00e9's view. A similarly rigid\npredetermination also limits the Kantian 'ideas of the reason' to a\ncertain set of principles whose guidance of the course of our\ntheoretical investigations is indeed only 'regulative,' but is 'a\npriori,' and so unchangeable. For M. Poincar\u00e9, on the contrary, all this\nadjustment of our interpretations of experience to the needs of our\nintellect is something far less rigid and unalterable, and is constantly\nsubject to the suggestions of experience. We must indeed interpret in\nour own way; but our way is itself only relatively determinate; it is\nessentially more or less plastic; other interpretations of experience\nare conceivable. Those that we use are merely the ones found to be most\nconvenient. But this convenience is not absolute necessity. Unverifiable\nand irrefutable hypotheses in science are indeed, in general,\nindispensable aids to the organization and to the guidance of our\ninterpretation of experience. But it is experience itself which points\nout to us what lines of interpretation will prove most convenient.\nInstead of Kant's rigid list of _a priori_ 'forms,' we consequently have\nin M. Poincar\u00e9's account a set of conventions, neither wholly subjective\nand arbitrary, nor yet imposed upon us unambiguously by the external\ncompulsion of experience. The organization of science, so far as this\norganization is due to hypotheses of the kind here in question, thus\nresembles that of a constitutional government--neither absolutely\nnecessary, nor yet determined apart from the will of the subjects, nor\nyet accidental--a free, yet not a capricious establishment of good\norder, in conformity with empirical needs.\n\nCharacteristic remains, however, for our author, as, in his decidedly\ncontrasting way, for Kant, the thought that _without principles which at\nevery stage transcend precise confirmation through such experience as is\nthen accessible the organization of experience is impossible_. Whether\none views these principles as conventions or as _a priori_ 'forms,' they\nmay therefore be described as hypotheses, but as hypotheses that, while\nlying at the basis of our actual physical sciences, at once refer to\nexperience and help us in dealing with experience, and are yet neither\nconfirmed nor refuted by the experiences which we possess or which we\ncan hope to attain.\n\nThree special instances or classes of instances, according to our\nauthor's account, may be used as illustrations of this general type of\nhypotheses. They are: (1) The hypothesis of the existence of continuous\nextensive _quanta_ in nature; (2) The principles of geometry; (3) The\nprinciples of mechanics and of the general theory of energy. In case of\neach of these special types of hypotheses we are at first disposed,\napart from reflection, to say that we _find_ the world to be thus or\nthus, so that, for instance, we can confirm the thesis according to\nwhich nature contains continuous magnitudes; or can prove or disprove\nthe physical truth of the postulates of Euclidean geometry; or can\nconfirm by definite experience the objective validity of the principles\nof mechanics. A closer examination reveals, according to our author, the\nincorrectness of all such opinions. Hypotheses of these various special\ntypes are needed; and their usefulness can be empirically shown. They\nare in touch with experience; and that they are not merely arbitrary\nconventions is also verifiable. They are not _a priori_ necessities; and\nwe can easily conceive intelligent beings whose experience could be best\ninterpreted without using these hypotheses. Yet these hypotheses are\n_not_ subject to direct confirmation or refutation by experience. They\nstand then in sharp contrast to the scientific hypotheses of the other,\nand more frequently recognized, type, _i. e._, to the hypotheses which\ncan be tested by a definite appeal to experience. To these other\nhypotheses our author attaches, of course, great importance. His\ntreatment of them is full of a living appreciation of the significance\nof empirical investigation. But the central problem of the logic of\nscience thus becomes the problem of the relation between the two\nfundamentally distinct types of hypotheses, _i. e._, between those which\ncan not be verified or refuted through experience, and those which can\nbe empirically tested.\n\n\nIV\n\nThe detailed treatment which M. Poincar\u00e9 gives to the problem thus\ndefined must be learned from his text. It is no part of my purpose to\nexpound, to defend or to traverse any of his special conclusions\nregarding this matter. Yet I can not avoid observing that, while M.\nPoincar\u00e9 strictly confines his illustrations and his expressions of\nopinion to those regions of science wherein, as special investigator, he\nis himself most at home, the issues which he thus raises regarding the\nlogic of science are of even more critical importance and of more\nimpressive interest when one applies M. Poincar\u00e9's methods to the study\nof the concepts and presuppositions of the organic and of the historical\nand social sciences, than when one confines one's attention, as our\nauthor here does, to the physical sciences. It belongs to the province\nof an introduction like the present to point out, however briefly and\ninadequately, that the significance of our author's ideas extends far\nbeyond the scope to which he chooses to confine their discussion.\n\nThe historical sciences, and in fact all those sciences such as geology,\nand such as the evolutionary sciences in general, undertake theoretical\nconstructions which relate to past time. Hypotheses relating to the more\nor less remote past stand, however, in a position which is very\ninteresting from the point of view of the logic of science. Directly\nspeaking, no such hypothesis is capable of confirmation or of\nrefutation, because we can not return into the past to verify by our own\nexperience what then happened. Yet indirectly, such hypotheses may lead\nto predictions of coming experience. These latter will be subject to\ncontrol. Thus, Schliemann's confidence that the legend of Troy had a\ndefinite historical foundation led to predictions regarding what certain\nexcavations would reveal. In a sense somewhat different from that which\nfilled Schliemann's enthusiastic mind, these predictions proved\nverifiable. The result has been a considerable change in the attitude\nof historians toward the legend of Troy. Geological investigation leads\nto predictions regarding the order of the strata or the course of\nmineral veins in a district, regarding the fossils which may be\ndiscovered in given formations, and so on. These hypotheses are subject\nto the control of experience. The various theories of evolutionary\ndoctrine include many hypotheses capable of confirmation and of\nrefutation by empirical tests. Yet, despite all such empirical control,\nit still remains true that whenever a science is mainly concerned with\nthe remote past, whether this science be archeology, or geology, or\nanthropology, or Old Testament history, the principal theoretical\nconstructions always include features which no appeal to present or to\naccessible future experience can ever definitely test. Hence the\nsuspicion with which students of experimental science often regard the\ntheoretical constructions of their confr\u00e8res of the sciences that deal\nwith the past. The origin of the races of men, of man himself, of life,\nof species, of the planet; the hypotheses of anthropologists, of\narcheologists, of students of 'higher criticism'--all these are matters\nwhich the men of the laboratory often regard with a general incredulity\nas belonging not at all to the domain of true science. Yet no one can\ndoubt the importance and the inevitableness of endeavoring to apply\nscientific method to these regions also. Science needs theories\nregarding the past history of the world. And no one who looks closer\ninto the methods of these sciences of past time can doubt that\nverifiable and unverifiable hypotheses are in all these regions\ninevitably interwoven; so that, while experience is always the guide,\nthe attitude of the investigator towards experience is determined by\ninterests which have to be partially due to what I should call that\n'internal meaning,' that human interest in rational theoretical\nconstruction which inspires the scientific inquiry; and the theoretical\nconstructions which prevail in such sciences are neither unbiased\nreports of the actual constitution of an external reality, nor yet\narbitrary constructions of fancy. These constructions in fact resemble\nin a measure those which M. Poincar\u00e9 in this book has analyzed in the\ncase of geometry. They are constructions molded, but _not_ predetermined\nin their details, by experience. We report facts; we let the facts\nspeak; but we, as we investigate, in the popular phrase, 'talk back' to\nthe facts. We interpret as well as report. Man is not merely made for\nscience, but science is made for man. It expresses his deepest\nintellectual needs, as well as his careful observations. It is an effort\nto bring internal meanings into harmony with external verifications. It\nattempts therefore to control, as well as to submit, to conceive with\nrational unity, as well as to accept data. Its arts are those directed\ntowards self-possession as well as towards an imitation of the outer\nreality which we find. It seeks therefore a disciplined freedom of\nthought. The discipline is as essential as the freedom; but the latter\nhas also its place. The theories of science are human, as well as\nobjective, internally rational, as well as (when that is possible)\nsubject to external tests.\n\nIn a field very different from that of the historical sciences, namely,\nin a science of observation and of experiment, which is at the same time\nan organic science, I have been led in the course of some study of the\nhistory of certain researches to notice the existence of a theoretical\nconception which has proved extremely fruitful in guiding research, but\nwhich apparently resembles in a measure the type of hypotheses of which\nM. Poincar\u00e9 speaks when he characterizes the principles of mechanics and\nof the theory of energy. I venture to call attention here to this\nconception, which seems to me to illustrate M. Poincar\u00e9's view of the\nfunctions of hypothesis in scientific work.\n\nThe modern science of pathology is usually regarded as dating from the\nearlier researches of Virchow, whose 'Cellular Pathology' was the\noutcome of a very careful and elaborate induction. Virchow, himself,\nfelt a strong aversion to mere speculation. He endeavored to keep close\nto observation, and to relieve medical science from the control of\nfantastic theories, such as those of the _Naturphilosophen_ had been.\nYet Virchow's researches were, as early as 1847, or still earlier,\nalready under the guidance of a theoretical presupposition which he\nhimself states as follows: \"We have learned to recognize,\" he says,\n\"that diseases are not autonomous organisms, that they are no entities\nthat have entered into the body, that they are no parasites which take\nroot in the body, but _that they merely show us the course of the vital\nprocesses under altered conditions_\" ('dasz sie nur Ablauf der\nLebenserscheinungen unter ver\u00e4nderten Bedingungen darstellen').\n\nThe enormous importance of this theoretical presupposition for all the\nearly successes of modern pathological investigation is generally\nrecognized by the experts. I do not doubt this opinion. It appears to be\na commonplace of the history of this science. But in Virchow's later\nyears this very presupposition seemed to some of his contemporaries to\nbe called in question by the successes of recent bacteriology. The\nquestion arose whether the theoretical foundations of Virchow's\npathology had not been set aside. And in fact the theory of the\nparasitical origin of a vast number of diseased conditions has indeed\ncome upon an empirical basis to be generally recognized. Yet to the end\nof his own career Virchow stoutly maintained that in all its essential\nsignificance his own fundamental principle remained quite untouched by\nthe newer discoveries. And, as a fact, this view could indeed be\nmaintained. For if diseases proved to be the consequences of the\npresence of parasites, the diseases themselves, so far as they belonged\nto the diseased organism, were still not the parasites, but were, as\nbefore, the reaction of the organism to the _ver\u00e4nderte Bedingungen_\nwhich the presence of the parasites entailed. So Virchow could well\ninsist. And if the famous principle in question is only stated with\nsufficient generality, it amounts simply to saying that if a disease\ninvolves a change in an organism, and if this change is subject to law\nat all, then the nature of the organism and the reaction of the organism\nto whatever it is which causes the disease must be understood in case\nthe disease is to be understood.\n\nFor this very reason, however, Virchow's theoretical principle in its\nmost general form _could be neither confirmed nor refuted by\nexperience_. It would remain empirically irrefutable, so far as I can\nsee, even if we should learn that the devil was the true cause of all\ndiseases. For the devil himself would then simply predetermine the\n_ver\u00e4nderte Bedingungen_ to which the diseased organism would be\nreacting. Let bullets or bacteria, poisons or compressed air, or the\ndevil be the _Bedingungen_ to which a diseased organism reacts, the\npostulate that Virchow states in the passage just quoted will remain\nirrefutable, if only this postulate be interpreted to meet the case. For\nthe principle in question merely says that whatever entity it may be,\nbullet, or poison, or devil, that affects the organism, the disease is\nnot that entity, but is the resulting alteration in the process of the\norganism.\n\nI insist, then, that this principle of Virchow's is no trial\nsupposition, no scientific hypothesis in the narrower sense--capable of\nbeing submitted to precise empirical tests. It is, on the contrary, a\nvery precious _leading idea_, a theoretical interpretation of phenomena,\nin the light of which observations are to be made--'a regulative\nprinciple' of research. It is equivalent to a resolution to search for\nthose detailed connections which link the processes of disease to the\nnormal process of the organism. Such a search undertakes to find the\ntrue unity, whatever that may prove to be, wherein the pathological and\nthe normal processes are linked. Now without some such leading idea, the\ncellular pathology itself could never have been reached; because the\nempirical facts in question would never have been observed. Hence this\nprinciple of Virchow's was indispensable to the growth of his science.\nYet it was not a verifiable and not a refutable hypothesis. One value of\nunverifiable and irrefutable hypotheses of this type lies, then, in the\nsort of empirical inquiries which they initiate, inspire, organize and\nguide. In these inquiries hypotheses in the narrower sense, that is,\ntrial propositions which are to be submitted to definite empirical\ncontrol, are indeed everywhere present. And the use of the other sort of\nprinciples lies wholly in their application to experience. Yet without\nwhat I have just proposed to call the 'leading ideas' of a science, that\nis, its principles of an unverifiable and irrefutable character,\nsuggested, but not to be finally tested, by experience, the hypotheses\nin the narrower sense would lack that guidance which, as M. Poincar\u00e9 has\nshown, the larger ideas of science give to empirical investigation.\n\n\nV\n\nI have dwelt, no doubt, at too great length upon one aspect only of our\nauthor's varied and well-balanced discussion of the problems and\nconcepts of scientific theory. Of the hypotheses in the narrower sense\nand of the value of direct empirical control, he has also spoken with\nthe authority and the originality which belong to his position. And in\ndealing with the foundations of mathematics he has raised one or two\nquestions of great philosophical import into which I have no time, even\nif I had the right, to enter here. In particular, in speaking of the\nessence of mathematical reasoning, and of the difficult problem of what\nmakes possible novel results in the field of pure mathematics, M.\nPoincar\u00e9 defends a thesis regarding the office of 'demonstration by\nrecurrence'--a thesis which is indeed disputable, which has been\ndisputed and which I myself should be disposed, so far as I at present\nunderstand the matter, to modify in some respects, even in accepting the\nspirit of our author's assertion. Yet there can be no doubt of the\nimportance of this thesis, and of the fact that it defines a\ncharacteristic that is indeed fundamental in a wide range of\nmathematical research. The philosophical problems that lie at the basis\nof recurrent proofs and processes are, as I have elsewhere argued, of\nthe most fundamental importance.\n\nThese, then, are a few hints relating to the significance of our\nauthor's discussion, and a few reasons for hoping that our own students\nwill profit by the reading of the book as those of other nations have\nalready done.\n\nOf the person and of the life-work of our author a few words are here,\nin conclusion, still in place, addressed, not to the students of his own\nscience, to whom his position is well known, but to the general reader\nwho may seek guidance in these pages.\n\nJules Henri Poincar\u00e9 was born at Nancy, in 1854, the son of a professor\nin the Faculty of Medicine at Nancy. He studied at the \u00c9cole\nPolytechnique and at the \u00c9cole des Mines, and later received his\ndoctorate in mathematics in 1879. In 1883 he began courses of\ninstruction in mathematics at the \u00c9cole Polytechnique; in 1886 received\na professorship of mathematical physics in the Faculty of Sciences at\nParis; then became member of the Academy of Sciences at Paris, in 1887,\nand devoted his life to instruction and investigation in the regions of\npure mathematics, of mathematical physics and of celestial mechanics.\nHis list of published treatises relating to various branches of his\nchosen sciences is long; and his original memoirs have included several\nmomentous investigations, which have gone far to transform more than one\nbranch of research. His presence at the International Congress of Arts\nand Science in St. Louis was one of the most noticeable features of that\nremarkable gathering of distinguished foreign guests. In Poincar\u00e9 the\nreader meets, then, not one who is primarily a speculative student of\ngeneral problems for their own sake, but an original investigator of the\nhighest rank in several distinct, although interrelated, branches of\nmodern research. The theory of functions--a highly recondite region of\npure mathematics--owes to him advances of the first importance, for\ninstance, the definition of a new type of functions. The 'problem of the\nthree bodies,' a famous and fundamental problem of celestial mechanics,\nhas received from his studies a treatment whose significance has been\nrecognized by the highest authorities. His international reputation has\nbeen confirmed by the conferring of more than one important prize for\nhis researches. His membership in the most eminent learned societies of\nvarious nations is widely extended; his volumes bearing upon various\nbranches of mathematics and of mathematical physics are used by special\nstudents in all parts of the learned world; in brief, he is, as\ngeometer, as analyst and as a theoretical physicist, a leader of his\nage.\n\nMeanwhile, as contributor to the philosophical discussion of the bases\nand methods of science, M. Poincar\u00e9 has long been active. When, in 1893,\nthe admirable _Revue de M\u00e9taphysique et de Morale_ began to appear, M.\nPoincar\u00e9 was soon found amongst the most satisfactory of the\ncontributors to the work of that journal, whose office it has especially\nbeen to bring philosophy and the various special sciences (both natural\nand moral) into a closer mutual understanding. The discussions brought\ntogether in the present volume are in large part the outcome of M.\nPoincar\u00e9's contributions to the _Revue de M\u00e9taphysique et de Morale_.\nThe reader of M. Poincar\u00e9's book is in presence, then, of a great\nspecial investigator who is also a philosopher.\n\n\n\n\nSCIENCE AND HYPOTHESIS\n\nINTRODUCTION\n\n\nFor a superficial observer, scientific truth is beyond the possibility\nof doubt; the logic of science is infallible, and if the scientists are\nsometimes mistaken, this is only from their mistaking its rules.\n\n\"The mathematical verities flow from a small number of self-evident\npropositions by a chain of impeccable reasonings; they impose themselves\nnot only on us, but on nature itself. They fetter, so to speak, the\nCreator and only permit him to choose between some relatively few\nsolutions. A few experiments then will suffice to let us know what\nchoice he has made. From each experiment a crowd of consequences will\nfollow by a series of mathematical deductions, and thus each experiment\nwill make known to us a corner of the universe.\"\n\nBehold what is for many people in the world, for scholars getting their\nfirst notions of physics, the origin of scientific certitude. This is\nwhat they suppose to be the r\u00f4le of experimentation and mathematics.\nThis same conception, a hundred years ago, was held by many savants who\ndreamed of constructing the world with as little as possible taken from\nexperiment.\n\nOn a little more reflection it was perceived how great a place\nhypothesis occupies; that the mathematician can not do without it, still\nless the experimenter. And then it was doubted if all these\nconstructions were really solid, and believed that a breath would\noverthrow them. To be skeptical in this fashion is still to be\nsuperficial. To doubt everything and to believe everything are two\nequally convenient solutions; each saves us from thinking.\n\nInstead of pronouncing a summary condemnation, we ought therefore to\nexamine with care the r\u00f4le of hypothesis; we shall then recognize, not\nonly that it is necessary, but that usually it is legitimate. We shall\nalso see that there are several sorts of hypotheses; that some are\nverifiable, and once confirmed by experiment become fruitful truths;\nthat others, powerless to lead us astray, may be useful to us in fixing\nour ideas; that others, finally, are hypotheses only in appearance and\nare reducible to disguised definitions or conventions.\n\nThese last are met with above all in mathematics and the related\nsciences. Thence precisely it is that these sciences get their rigor;\nthese conventions are the work of the free activity of our mind, which,\nin this domain, recognizes no obstacle. Here our mind can affirm, since\nit decrees; but let us understand that while these decrees are imposed\nupon _our_ science, which, without them, would be impossible, they are\nnot imposed upon nature. Are they then arbitrary? No, else were they\nsterile. Experiment leaves us our freedom of choice, but it guides us by\naiding us to discern the easiest way. Our decrees are therefore like\nthose of a prince, absolute but wise, who consults his council of state.\n\nSome people have been struck by this character of free convention\nrecognizable in certain fundamental principles of the sciences. They\nhave wished to generalize beyond measure, and, at the same time, they\nhave forgotten that liberty is not license. Thus they have reached what\nis called _nominalism_, and have asked themselves if the savant is not\nthe dupe of his own definitions and if the world he thinks he discovers\nis not simply created by his own caprice.[1] Under these conditions\nscience would be certain, but deprived of significance.\n\n [1] See Le Roy, 'Science et Philosophie,' _Revue de M\u00e9taphysique\n et de Morale_, 1901.\n\nIf this were so, science would be powerless. Now every day we see it\nwork under our very eyes. That could not be if it taught us nothing of\nreality. Still, the things themselves are not what it can reach, as the\nna\u00efve dogmatists think, but only the relations between things. Outside\nof these relations there is no knowable reality.\n\nSuch is the conclusion to which we shall come, but for that we must\nreview the series of sciences from arithmetic and geometry to mechanics\nand experimental physics.\n\nWhat is the nature of mathematical reasoning? Is is really deductive, as\nis commonly supposed? A deeper analysis shows us that it is not, that it\npartakes in a certain measure of the nature of inductive reasoning, and\njust because of this is it so fruitful. None the less does it retain its\ncharacter of rigor absolute; this is the first thing that had to be\nshown.\n\nKnowing better now one of the instruments which mathematics puts into\nthe hands of the investigator, we had to analyze another fundamental\nnotion, that of mathematical magnitude. Do we find it in nature, or do\nwe ourselves introduce it there? And, in this latter case, do we not\nrisk marring everything? Comparing the rough data of our senses with\nthat extremely complex and subtile concept which mathematicians call\nmagnitude, we are forced to recognize a difference; this frame into\nwhich we wish to force everything is of our own construction; but we\nhave not made it at random. We have made it, so to speak, by measure and\ntherefore we can make the facts fit into it without changing what is\nessential in them.\n\nAnother frame which we impose on the world is space. Whence come the\nfirst principles of geometry? Are they imposed on us by logic?\nLobachevski has proved not, by creating non-Euclidean geometry. Is space\nrevealed to us by our senses? Still no, for the space our senses could\nshow us differs absolutely from that of the geometer. Is experience the\nsource of geometry? A deeper discussion will show us it is not. We\ntherefore conclude that the first principles of geometry are only\nconventions; but these conventions are not arbitrary and if transported\ninto another world (that I call the non-Euclidean world and seek to\nimagine), then we should have been led to adopt others.\n\nIn mechanics we should be led to analogous conclusions, and should see\nthat the principles of this science, though more directly based on\nexperiment, still partake of the conventional character of the geometric\npostulates. Thus far nominalism triumphs; but now we arrive at the\nphysical sciences, properly so called. Here the scene changes; we meet\nanother sort of hypotheses and we see their fertility. Without doubt, at\nfirst blush, the theories seem to us fragile, and the history of science\nproves to us how ephemeral they are; yet they do not entirely perish,\nand of each of them something remains. It is this something we must seek\nto disentangle, since there and there alone is the veritable reality.\n\nThe method of the physical sciences rests on the induction which makes\nus expect the repetition of a phenomenon when the circumstances under\nwhich it first happened are reproduced. If _all_ these circumstances\ncould be reproduced at once, this principle could be applied without\nfear; but that will never happen; some of these circumstances will\nalways be lacking. Are we absolutely sure they are unimportant?\nEvidently not. That may be probable, it can not be rigorously certain.\nHence the important r\u00f4le the notion of probability plays in the physical\nsciences. The calculus of probabilities is therefore not merely a\nrecreation or a guide to players of baccarat, and we must seek to go\ndeeper with its foundations. Under this head I have been able to give\nonly very incomplete results, so strongly does this vague instinct which\nlets us discern probability defy analysis.\n\nAfter a study of the conditions under which the physicist works, I have\nthought proper to show him at work. For that I have taken instances from\nthe history of optics and of electricity. We shall see whence have\nsprung the ideas of Fresnel, of Maxwell, and what unconscious hypotheses\nwere made by Amp\u00e8re and the other founders of electrodynamics.\n\n\n\n\nPART I\n\n\nNUMBER AND MAGNITUDE\n\n\n\n\nCHAPTER I\n\nON THE NATURE OF MATHEMATICAL REASONING\n\n\nI\n\nThe very possibility of the science of mathematics seems an insoluble\ncontradiction. If this science is deductive only in appearance, whence\ndoes it derive that perfect rigor no one dreams of doubting? If, on the\ncontrary, all the propositions it enunciates can be deduced one from\nanother by the rules of formal logic, why is not mathematics reduced to\nan immense tautology? The syllogism can teach us nothing essentially\nnew, and, if everything is to spring from the principle of identity,\neverything should be capable of being reduced to it. Shall we then admit\nthat the enunciations of all those theorems which fill so many volumes\nare nothing but devious ways of saying _A_ is _A_?\n\nWithout doubt, we can go back to the axioms, which are at the source of\nall these reasonings. If we decide that these can not be reduced to the\nprinciple of contradiction, if still less we see in them experimental\nfacts which could not partake of mathematical necessity, we have yet the\nresource of classing them among synthetic _a priori_ judgments. This is\nnot to solve the difficulty, but only to baptize it; and even if the\nnature of synthetic judgments were for us no mystery, the contradiction\nwould not have disappeared, it would only have moved back; syllogistic\nreasoning remains incapable of adding anything to the data given it:\nthese data reduce themselves to a few axioms, and we should find nothing\nelse in the conclusions.\n\nNo theorem could be new if no new axiom intervened in its demonstration;\nreasoning could give us only the immediately evident verities borrowed\nfrom direct intuition; it would be only an intermediary parasite, and\ntherefore should we not have good reason to ask whether the whole\nsyllogistic apparatus did not serve solely to disguise our borrowing?\n\nThe contradiction will strike us the more if we open any book on\nmathematics; on every page the author will announce his intention of\ngeneralizing some proposition already known. Does the mathematical\nmethod proceed from the particular to the general, and, if so, how then\ncan it be called deductive?\n\nIf finally the science of number were purely analytic, or could be\nanalytically derived from a small number of synthetic judgments, it\nseems that a mind sufficiently powerful could at a glance perceive all\nits truths; nay more, we might even hope that some day one would invent\nto express them a language sufficiently simple to have them appear\nself-evident to an ordinary intelligence.\n\nIf we refuse to admit these consequences, it must be conceded that\nmathematical reasoning has of itself a sort of creative virtue and\nconsequently differs from the syllogism.\n\nThe difference must even be profound. We shall not, for example, find\nthe key to the mystery in the frequent use of that rule according to\nwhich one and the same uniform operation applied to two equal numbers\nwill give identical results.\n\nAll these modes of reasoning, whether or not they be reducible to the\nsyllogism properly so called, retain the analytic character, and just\nbecause of that are powerless.\n\n\nII\n\nThe discussion is old; Leibnitz tried to prove 2 and 2 make 4; let us\nlook a moment at his demonstration.\n\nI will suppose the number 1 defined and also the operation _x_ + 1 which\nconsists in adding unity to a given number _x_.\n\nThese definitions, whatever they be, do not enter into the course of the\nreasoning.\n\nI define then the numbers 2, 3 and 4 by the equalities\n\n (1) 1 + 1 = 2; (2) 2 + 1 = 3; (3) 3 + 1 = 4.\n\nIn the same way, I define the operation _x_ + 2 by the relation:\n\n (4) _x_ + 2 = (_x_ + 1) + 1.\n\nThat presupposed, we have\n\n 2 + 1 + 1 = 3 + 1 (Definition 2),\n 3 + 1 = 4 (Definition 3),\n 2 + 2 = (2 + 1) + 1 (Definition 4),\n\nwhence\n\n 2 + 2 = 4 Q.E.D.\n\nIt can not be denied that this reasoning is purely analytic. But ask any\nmathematician: 'That is not a demonstration properly so called,' he will\nsay to you: 'that is a verification.' We have confined ourselves to\ncomparing two purely conventional definitions and have ascertained their\nidentity; we have learned nothing new. _Verification_ differs from true\ndemonstration precisely because it is purely analytic and because it is\nsterile. It is sterile because the conclusion is nothing but the\npremises translated into another language. On the contrary, true\ndemonstration is fruitful because the conclusion here is in a sense more\ngeneral than the premises.\n\nThe equality 2 + 2 = 4 is thus susceptible of a verification only\nbecause it is particular. Every particular enunciation in mathematics\ncan always be verified in this same way. But if mathematics could be\nreduced to a series of such verifications, it would not be a science. So\na chess-player, for example, does not create a science in winning a\ngame. There is no science apart from the general.\n\nIt may even be said the very object of the exact sciences is to spare us\nthese direct verifications.\n\n\nIII\n\nLet us, therefore, see the geometer at work and seek to catch his\nprocess.\n\nThe task is not without difficulty; it does not suffice to open a work\nat random and analyze any demonstration in it.\n\nWe must first exclude geometry, where the question is complicated by\narduous problems relative to the r\u00f4le of the postulates, to the nature\nand the origin of the notion of space. For analogous reasons we can not\nturn to the infinitesimal analysis. We must seek mathematical thought\nwhere it has remained pure, that is, in arithmetic.\n\nA choice still is necessary; in the higher parts of the theory of\nnumbers, the primitive mathematical notions have already undergone an\nelaboration so profound that it becomes difficult to analyze them.\n\nIt is, therefore, at the beginning of arithmetic that we must expect to\nfind the explanation we seek, but it happens that precisely in the\ndemonstration of the most elementary theorems the authors of the classic\ntreatises have shown the least precision and rigor. We must not impute\nthis to them as a crime; they have yielded to a necessity; beginners are\nnot prepared for real mathematical rigor; they would see in it only\nuseless and irksome subtleties; it would be a waste of time to try\nprematurely to make them more exacting; they must pass over rapidly, but\nwithout skipping stations, the road traversed slowly by the founders of\nthe science.\n\nWhy is so long a preparation necessary to become habituated to this\nperfect rigor, which, it would seem, should naturally impress itself\nupon all good minds? This is a logical and psychological problem well\nworthy of study.\n\nBut we shall not take it up; it is foreign to our purpose; all I wish to\ninsist on is that, not to fail of our purpose, we must recast the\ndemonstrations of the most elementary theorems and give them, not the\ncrude form in which they are left, so as not to harass beginners, but\nthe form that will satisfy a skilled geometer.\n\nDEFINITION OF ADDITION.--I suppose already defined the operation\n_x_ + 1, which consists in adding the number 1 to a given number _x_.\n\nThis definition, whatever it be, does not enter into our subsequent\nreasoning.\n\nWe now have to define the operation _x_ + _a_, which consists in adding\nthe number _a_ to a given number _x_.\n\nSupposing we have defined the operation\n\n _x_ + (_a_ - 1),\n\nthe operation _x_ + _a_ will be defined by the equality\n\n (1) _x_ + _a_ = [_x_ + (_a_ - 1)] + 1.\n\nWe shall know then what _x + a_ is when we know what _x_ + (_a_ - 1)\nis, and as I have supposed that to start with we knew what _x_ + 1 is,\nwe can define successively and 'by recurrence' the operations _x_ + 2,\n_x_ + 3, etc.\n\nThis definition deserves a moment's attention; it is of a particular\nnature which already distinguishes it from the purely logical\ndefinition; the equality (1) contains an infinity of distinct\ndefinitions, each having a meaning only when one knows the preceding.\n\nPROPERTIES OF ADDITION.--_Associativity._--I say that\n\n _a_ + (_b_ + _c_) = (_a_ + _b_) + _c_.\n\nIn fact the theorem is true for _c_ = 1; it is then written\n\n _a_ + (_b_ + 1) = (_a_ + _b_) + 1,\n\nwhich, apart from the difference of notation, is nothing but the\nequality (1), by which I have just defined addition.\n\nSupposing the theorem true for _c_ = [gamma], I say it will be true for\n_c_ = [gamma] + 1.\n\nIn fact, supposing\n\n (_a_ + _b_) + [gamma] = _a_ + (_b_ + [gamma]),\n\nit follows that\n\n [(_a_ + _b_) + [gamma]] + 1 = [_a_ + (_b_ + [gamma])] + 1\n\nor by definition (1)\n\n (_a_ + _b_) + ([gamma] + 1) = _a_ + (_b_ + [gamma] + 1)\n = _a_ + [_b_ + ([gamma] + 1)],\n\nwhich shows, by a series of purely analytic deductions, that the\ntheorem is true for [gamma] + 1.\n\nBeing true for _c_ = 1, we thus see successively that so it is for\n_c_ = 2, for _c_ = 3, etc.\n\n_Commutativity._--1\u00ba I say that\n\n _a_ + 1 = 1 + _a_.\n\nThe theorem is evidently true for _a_ = 1; we can _verify_ by purely\nanalytic reasoning that if it is true for _a_ = [gamma] it will be true\nfor _a_ = [gamma] + 1; for then\n\n ([gamma] + 1) + 1 = (1 + [gamma]) + 1 = 1 + ([gamma] + 1);\n\nnow it is true for _a_ = 1, therefore it will be true for _a_ = 2, for\n_a_ = 3, etc., which is expressed by saying that the enunciated\nproposition is demonstrated by recurrence.\n\n2\u00ba I say that\n\n _a_ + _b_ = _b_ + _a_.\n\nThe theorem has just been demonstrated for _b_ = 1; it can be verified\nanalytically that if it is true for _b_ = [beta], it will be true for\n_b_ = [beta] + 1.\n\nThe proposition is therefore established by recurrence.\n\nDEFINITION OF MULTIPLICATION.--We shall define multiplication by the\nequalities.\n\n (1) _a_ \u00d7 1 = _a_.\n\n (2) _a_ \u00d7 _b_ = [_a_ \u00d7 (_b_ - 1)] + _a_.\n\nLike equality (1), equality (2) contains an infinity of definitions;\nhaving defined a \u00d7 1, it enables us to define successively: _a_ \u00d7 2,\n_a_ \u00d7 3, etc.\n\nPROPERTIES OF MULTIPLICATION.--_Distributivity._--I say that\n\n (_a_ + _b_) \u00d7 _c_ = (_a_ \u00d7 _c_) + (_b_ \u00d7 _c_).\n\nWe verify analytically that the equality is true for _c_ = 1; then\nthat if the theorem is true for _c_ = [gamma], it will be true\nfor _c_ = [gamma] + 1.\n\nThe proposition is, therefore, demonstrated by recurrence.\n\n_Commutativity._--1\u00ba I say that\n\n _a_ \u00d7 1 = 1 \u00d7 _a_.\n\nThe theorem is evident for _a_ = 1.\n\nWe verify analytically that if it is true for _a_ = [alpha], it will be\ntrue for _a_ = [alpha] + 1.\n\n2\u00ba I say that\n\n _a_ \u00d7 _b_ = _b_ \u00d7 _a_.\n\nThe theorem has just been proven for _b_ = 1. We could verify\nanalytically that if it is true for _b_ = [beta], it will be true\nfor _b_ = [beta] + 1.\n\n\nIV\n\nHere I stop this monotonous series of reasonings. But this very monotony\nhas the better brought out the procedure which is uniform and is met\nagain at each step.\n\nThis procedure is the demonstration by recurrence. We first establish a\ntheorem for _n_ = 1; then we show that if it is true of _n_ - 1, it is\ntrue of _n_, and thence conclude that it is true for all the whole\nnumbers.\n\nWe have just seen how it may be used to demonstrate the rules of\naddition and multiplication, that is to say, the rules of the algebraic\ncalculus; this calculus is an instrument of transformation, which lends\nitself to many more differing combinations than does the simple\nsyllogism; but it is still an instrument purely analytic, and incapable\nof teaching us anything new. If mathematics had no other instrument, it\nwould therefore be forthwith arrested in its development; but it has\nrecourse anew to the same procedure, that is, to reasoning by\nrecurrence, and it is able to continue its forward march.\n\nIf we look closely, at every step we meet again this mode of reasoning,\neither in the simple form we have just given it, or under a form more or\nless modified.\n\nHere then we have the mathematical reasoning _par excellence_, and we\nmust examine it more closely.\n\n\nV\n\nThe essential characteristic of reasoning by recurrence is that it\ncontains, condensed, so to speak, in a single formula, an infinity of\nsyllogisms.\n\nThat this may the better be seen, I will state one after another these\nsyllogisms which are, if you will allow me the expression, arranged in\n'cascade.'\n\nThese are of course hypothetical syllogisms.\n\nThe theorem is true of the number 1.\n\nNow, if it is true of 1, it is true of 2.\n\nTherefore it is true of 2.\n\nNow, if it is true of 2, it is true of 3.\n\nTherefore it is true of 3, and so on.\n\nWe see that the conclusion of each syllogism serves as minor to the\nfollowing.\n\nFurthermore the majors of all our syllogisms can be reduced to a single\nformula.\n\nIf the theorem is true of _n_ - 1, so it is of _n_.\n\nWe see, then, that in reasoning by recurrence we confine ourselves to\nstating the minor of the first syllogism, and the general formula which\ncontains as particular cases all the majors.\n\nThis never-ending series of syllogisms is thus reduced to a phrase of a\nfew lines.\n\nIt is now easy to comprehend why every particular consequence of a\ntheorem can, as I have explained above, be verified by purely analytic\nprocedures.\n\nIf instead of showing that our theorem is true of all numbers, we only\nwish to show it true of the number 6, for example, it will suffice for\nus to establish the first 5 syllogisms of our cascade; 9 would be\nnecessary if we wished to prove the theorem for the number 10; more\nwould be needed for a larger number; but, however great this number\nmight be, we should always end by reaching it, and the analytic\nverification would be possible.\n\nAnd yet, however far we thus might go, we could never rise to the\ngeneral theorem, applicable to all numbers, which alone can be the\nobject of science. To reach this, an infinity of syllogisms would be\nnecessary; it would be necessary to overleap an abyss that the patience\nof the analyst, restricted to the resources of formal logic alone, never\ncould fill up.\n\nI asked at the outset why one could not conceive of a mind sufficiently\npowerful to perceive at a glance the whole body of mathematical truths.\n\nThe answer is now easy; a chess-player is able to combine four moves,\nfive moves, in advance, but, however extraordinary he may be, he will\nnever prepare more than a finite number of them; if he applies his\nfaculties to arithmetic, he will not be able to perceive its general\ntruths by a single direct intuition; to arrive at the smallest theorem\nhe can not dispense with the aid of reasoning by recurrence, for this is\nan instrument which enables us to pass from the finite to the infinite.\n\nThis instrument is always useful, for, allowing us to overleap at a\nbound as many stages as we wish, it spares us verifications, long,\nirksome and monotonous, which would quickly become impracticable. But it\nbecomes indispensable as soon as we aim at the general theorem, to which\nanalytic verification would bring us continually nearer without ever\nenabling us to reach it.\n\nIn this domain of arithmetic, we may think ourselves very far from the\ninfinitesimal analysis, and yet, as we have just seen, the idea of the\nmathematical infinite already plays a preponderant r\u00f4le, and without it\nthere would be no science, because there would be nothing general.\n\n\nVI\n\nThe judgment on which reasoning by recurrence rests can be put under\nother forms; we may say, for example, that in an infinite collection of\ndifferent whole numbers there is always one which is less than all the\nothers.\n\nWe can easily pass from one enunciation to the other and thus get the\nillusion of having demonstrated the legitimacy of reasoning by\nrecurrence. But we shall always be arrested, we shall always arrive at\nan undemonstrable axiom which will be in reality only the proposition to\nbe proved translated into another language.\n\nWe can not therefore escape the conclusion that the rule of reasoning by\nrecurrence is irreducible to the principle of contradiction.\n\nNeither can this rule come to us from experience; experience could teach\nus that the rule is true for the first ten or hundred numbers; for\nexample, it can not attain to the indefinite series of numbers, but only\nto a portion of this series, more or less long but always limited.\n\nNow if it were only a question of that, the principle of contradiction\nwould suffice; it would always allow of our developing as many\nsyllogisms as we wished; it is only when it is a question of including\nan infinity of them in a single formula, it is only before the infinite\nthat this principle fails, and there too, experience becomes powerless.\nThis rule, inaccessible to analytic demonstration and to experience, is\nthe veritable type of the synthetic _a priori_ judgment. On the other\nhand, we can not think of seeing in it a convention, as in some of the\npostulates of geometry.\n\nWhy then does this judgment force itself upon us with an irresistible\nevidence? It is because it is only the affirmation of the power of the\nmind which knows itself capable of conceiving the indefinite repetition\nof the same act when once this act is possible. The mind has a direct\nintuition of this power, and experience can only give occasion for using\nit and thereby becoming conscious of it.\n\nBut, one will say, if raw experience can not legitimatize reasoning by\nrecurrence, is it so of experiment aided by induction? We see\nsuccessively that a theorem is true of the number 1, of the number 2, of\nthe number 3 and so on; the law is evident, we say, and it has the same\nwarranty as every physical law based on observations, whose number is\nvery great but limited.\n\nHere is, it must be admitted, a striking analogy with the usual\nprocedures of induction. But there is an essential difference. Induction\napplied to the physical sciences is always uncertain, because it rests\non the belief in a general order of the universe, an order outside of\nus. Mathematical induction, that is, demonstration by recurrence, on the\ncontrary, imposes itself necessarily because it is only the affirmation\nof a property of the mind itself.\n\n\nVII\n\nMathematicians, as I have said before, always endeavor to _generalize_\nthe propositions they have obtained, and, to seek no other example, we\nhave just proved the equality:\n\n _a_ + 1 = 1 + _a_\n\nand afterwards used it to establish the equality\n\n _a_ + _b_ = _b_ + _a_\n\nwhich is manifestly more general.\n\nMathematics can, therefore, like the other sciences, proceed from the\nparticular to the general.\n\nThis is a fact which would have appeared incomprehensible to us at the\noutset of this study, but which is no longer mysterious to us, since we\nhave ascertained the analogies between demonstration by recurrence and\nordinary induction.\n\nWithout doubt recurrent reasoning in mathematics and inductive reasoning\nin physics rest on different foundations, but their march is parallel,\nthey advance in the same sense, that is to say, from the particular to\nthe general.\n\nLet us examine the case a little more closely.\n\nTo demonstrate the equality\n\n _a_ + 2 = 2 + _a_\n\nit suffices to twice apply the rule\n\n (1) _a_ + 1 = 1 + _a_\n\nand write\n\n (2) _a_ + 2 = _a_ + 1 + 1 = 1 + _a_ + 1 = 1 + 1 + _a_ = 2 + _a_.\n\nThe equality (2) thus deduced in purely analytic way from the equality\n(1) is, however, not simply a particular ease of it; it is something\nquite different.\n\nWe can not therefore even say that in the really analytic and deductive\npart of mathematical reasoning we proceed from the general to the\nparticular in the ordinary sense of the word.\n\nThe two members of the equality (2) are simply combinations more\ncomplicated than the two members of the equality (1), and analysis only\nserves to separate the elements which enter into these combinations and\nto study their relations.\n\nMathematicians proceed therefore 'by construction,' they 'construct'\ncombinations more and more complicated. Coming back then by the analysis\nof these combinations, of these aggregates, so to speak, to their\nprimitive elements, they perceive the relations of these elements and\nfrom them deduce the relations of the aggregates themselves.\n\nThis is a purely analytical proceeding, but it is not, however, a\nproceeding from the general to the particular, because evidently the\naggregates can not be regarded as more particular than their elements.\n\nGreat importance, and justly, has been attached to this procedure of\n'construction,' and some have tried to see in it the necessary and\nsufficient condition for the progress of the exact sciences.\n\nNecessary, without doubt; but sufficient, no.\n\nFor a construction to be useful and not a vain toil for the mind, that\nit may serve as stepping-stone to one wishing to mount, it must first of\nall possess a sort of unity enabling us to see in it something besides\nthe juxtaposition of its elements.\n\nOr, more exactly, there must be some advantage in considering the\nconstruction rather than its elements themselves.\n\nWhat can this advantage be?\n\nWhy reason on a polygon, for instance, which is always decomposable into\ntriangles, and not on the elementary triangles?\n\nIt is because there are properties appertaining to polygons of any\nnumber of sides and that may be immediately applied to any particular\npolygon.\n\nUsually, on the contrary, it is only at the cost of the most prolonged\nexertions that they could be found by studying directly the relations of\nthe elementary triangles. The knowledge of the general theorem spares us\nthese efforts.\n\nA construction, therefore, becomes interesting only when it can be\nranged beside other analogous constructions, forming species of the same\ngenus.\n\nIf the quadrilateral is something besides the juxtaposition of two\ntriangles, this is because it belongs to the genus polygon.\n\nMoreover, one must be able to demonstrate the properties of the genus\nwithout being forced to establish them successively for each of the\nspecies.\n\nTo attain that, we must necessarily mount from the particular to the\ngeneral, ascending one or more steps.\n\nThe analytic procedure 'by construction' does not oblige us to descend,\nbut it leaves us at the same level.\n\nWe can ascend only by mathematical induction, which alone can teach us\nsomething new. Without the aid of this induction, different in certain\nrespects from physical induction, but quite as fertile, construction\nwould be powerless to create science.\n\nObserve finally that this induction is possible only if the same\noperation can be repeated indefinitely. That is why the theory of chess\ncan never become a science, for the different moves of the same game do\nnot resemble one another.\n\n\n\n\nCHAPTER II\n\nMATHEMATICAL MAGNITUDE AND EXPERIENCE\n\n\nTo learn what mathematicians understand by a continuum, one should not\ninquire of geometry. The geometer always seeks to represent to himself\nmore or less the figures he studies, but his representations are for him\nonly instruments; in making geometry he uses space just as he does\nchalk; so too much weight should not be attached to non-essentials,\noften of no more importance than the whiteness of the chalk.\n\nThe pure analyst has not this rock to fear. He has disengaged the\nscience of mathematics from all foreign elements, and can answer our\nquestion: 'What exactly is this continuum about which mathematicians\nreason?' Many analysts who reflect on their art have answered already;\nMonsieur Tannery, for example, in his _Introduction \u00e0 la th\u00e9orie des\nfonctions d'une variable_.\n\nLet us start from the scale of whole numbers; between two consecutive\nsteps, intercalate one or more intermediary steps, then between these\nnew steps still others, and so on indefinitely. Thus we shall have an\nunlimited number of terms; these will be the numbers called fractional,\nrational or commensurable. But this is not yet enough; between these\nterms, which, however, are already infinite in number, it is still\nnecessary to intercalate others called irrational or incommensurable. A\nremark before going further. The continuum so conceived is only a\ncollection of individuals ranged in a certain order, infinite in number,\nit is true, but _exterior_ to one another. This is not the ordinary\nconception, wherein is supposed between the elements of the continuum a\nsort of intimate bond which makes of them a whole, where the point does\nnot exist before the line, but the line before the point. Of the\ncelebrated formula, 'the continuum is unity in multiplicity,' only the\nmultiplicity remains, the unity has disappeared. The analysts are none\nthe less right in defining their continuum as they do, for they always\nreason on just this as soon as they pique themselves on their rigor. But\nthis is enough to apprise us that the veritable mathematical continuum\nis a very different thing from that of the physicists and that of the\nmetaphysicians.\n\nIt may also be said perhaps that the mathematicians who are content with\nthis definition are dupes of words, that it is necessary to say\nprecisely what each of these intermediary steps is, to explain how they\nare to be intercalated and to demonstrate that it is possible to do it.\nBut that would be wrong; the only property of these steps which is used\nin their reasonings[2] is that of being before or after such and such\nsteps; therefore also this alone should occur in the definition.\n\n [2] With those contained in the special conventions which serve to\n define addition and of which we shall speak later.\n\nSo how the intermediary terms should be intercalated need not concern\nus; on the other hand, no one will doubt the possibility of this\noperation, unless from forgetting that possible, in the language of\ngeometers, simply means free from contradiction.\n\nOur definition, however, is not yet complete, and I return to it after\nthis over-long digression.\n\nDEFINITION OF INCOMMENSURABLES.--The mathematicians of the Berlin\nschool, Kronecker in particular, have devoted themselves to constructing\nthis continuous scale of fractional and irrational numbers without using\nany material other than the whole number. The mathematical continuum\nwould be, in this view, a pure creation of the mind, where experience\nwould have no part.\n\nThe notion of the rational number seeming to them to present no\ndifficulty, they have chiefly striven to define the incommensurable\nnumber. But before producing here their definition, I must make a remark\nto forestall the astonishment it is sure to arouse in readers unfamiliar\nwith the customs of geometers.\n\nMathematicians study not objects, but relations between objects; the\nreplacement of these objects by others is therefore indifferent to them,\nprovided the relations do not change. The matter is for them\nunimportant, the form alone interests them.\n\nWithout recalling this, it would scarcely be comprehensible that\nDedekind should designate by the name _incommensurable number_ a mere\nsymbol, that is to say, something very different from the ordinary idea\nof a quantity, which should be measurable and almost tangible.\n\nLet us see now what Dedekind's definition is:\n\nThe commensurable numbers can in an infinity of ways be partitioned into\ntwo classes, such that any number of the first class is greater than any\nnumber of the second class.\n\nIt may happen that among the numbers of the first class there is one\nsmaller than all the others; if, for example, we range in the first\nclass all numbers greater than 2, and 2 itself, and in the second class\nall numbers less than 2, it is clear that 2 will be the least of all\nnumbers of the first class. The number 2 may be chosen as symbol of this\npartition.\n\nIt may happen, on the contrary, that among the numbers of the second\nclass is one greater than all the others; this is the case, for example,\nif the first class comprehends all numbers greater than 2, and the\nsecond all numbers less than 2, and 2 itself. Here again the number 2\nmay be chosen as symbol of this partition.\n\nBut it may equally well happen that neither is there in the first class\na number less than all the others, nor in the second class a number\ngreater than all the others. Suppose, for example, we put in the first\nclass all commensurable numbers whose squares are greater than 2 and in\nthe second all whose squares are less than 2. There is none whose square\nis precisely 2. Evidently there is not in the first class a number less\nthan all the others, for, however near the square of a number may be to\n2, we can always find a commensurable number whose square is still\ncloser to 2.\n\nIn Dedekind's view, the incommensurable number\n\n sqrt(2) or (2)^{1/2}\n\nis nothing but the symbol of this particular mode of partition of\ncommensurable numbers; and to each mode of partition corresponds thus a\nnumber, commensurable or not, which serves as its symbol.\n\nBut to be content with this would be to forget too far the origin of\nthese symbols; it remains to explain how we have been led to attribute\nto them a sort of concrete existence, and, besides, does not the\ndifficulty begin even for the fractional numbers themselves? Should we\nhave the notion of these numbers if we had not previously known a matter\nthat we conceive as infinitely divisible, that is to say, a continuum?\n\nTHE PHYSICAL CONTINUUM.--We ask ourselves then if the notion of the\nmathematical continuum is not simply drawn from experience. If it were,\nthe raw data of experience, which are our sensations, would be\nsusceptible of measurement. We might be tempted to believe they really\nare so, since in these latter days the attempt has been made to measure\nthem and a law has even been formulated, known as Fechner's law,\naccording to which sensation is proportional to the logarithm of the\nstimulus.\n\nBut if we examine more closely the experiments by which it has been\nsought to establish this law, we shall be led to a diametrically\nopposite conclusion. It has been observed, for example, that a weight\n_A_ of 10 grams and a weight _B_ of 11 grams produce identical\nsensations, that the weight _B_ is just as indistinguishable from a\nweight _C_ of 12 grams, but that the weight _A_ is easily distinguished\nfrom the weight _C_. Thus the raw results of experience may be expressed\nby the following relations:\n\n _A_ =_B_, _B_ = _C_, _A_ < _C_,\n\nwhich may be regarded as the formula of the physical continuum.\n\nBut here is an intolerable discord with the principle of contradiction,\nand the need of stopping this has compelled us to invent the\nmathematical continuum.\n\nWe are, therefore, forced to conclude that this notion has been created\nentirely by the mind, but that experience has given the occasion.\n\nWe can not believe that two quantities equal to a third are not equal to\none another, and so we are led to suppose that _A_ is different from _B_\nand _B_ from _C_, but that the imperfection of our senses has not\npermitted of our distinguishing them.\n\nCREATION OF THE MATHEMATICAL CONTINUUM.--_First Stage._ So far it would\nsuffice, in accounting for the facts, to intercalate between _A_ and _B_\na few terms, which would remain discrete. What happens now if we have\nrecourse to some instrument to supplement the feebleness of our senses,\nif, for example, we make use of a microscope? Terms such as _A_ and _B_,\nbefore indistinguishable, appear now distinct; but between _A_ and _B_,\nnow become distinct, will be intercalated a new term, _D_, that we can\ndistinguish neither from _A_ nor from _B_. Despite the employment of the\nmost highly perfected methods, the raw results of our experience will\nalways present the characteristics of the physical continuum with the\ncontradiction which is inherent in it.\n\nWe shall escape it only by incessantly intercalating new terms between\nthe terms already distinguished, and this operation must be continued\nindefinitely. We might conceive the stopping of this operation if we\ncould imagine some instrument sufficiently powerful to decompose the\nphysical continuum into discrete elements, as the telescope resolves the\nmilky way into stars. But this we can not imagine; in fact, it is with\nthe eye we observe the image magnified by the microscope, and\nconsequently this image must always retain the characteristics of visual\nsensation and consequently those of the physical continuum.\n\nNothing distinguishes a length observed directly from the half of this\nlength doubled by the microscope. The whole is homogeneous with the\npart; this is a new contradiction, or rather it would be if the number\nof terms were supposed finite; in fact, it is clear that the part\ncontaining fewer terms than the whole could not be similar to the whole.\n\nThe contradiction ceases when the number of terms is regarded as\ninfinite; nothing hinders, for example, considering the aggregate of\nwhole numbers as similar to the aggregate of even numbers, which,\nhowever, is only a part of it; and, in fact, to each whole number\ncorresponds an even number, its double.\n\nBut it is not only to escape this contradiction contained in the\nempirical data that the mind is led to create the concept of a\ncontinuum, formed of an indefinite number of terms.\n\nAll happens as in the sequence of whole numbers. We have the faculty of\nconceiving that a unit can be added to a collection of units; thanks to\nexperience, we have occasion to exercise this faculty and we become\nconscious of it; but from this moment we feel that our power has no\nlimit and that we can count indefinitely, though we have never had to\ncount more than a finite number of objects.\n\nJust so, as soon as we have been led to intercalate means between two\nconsecutive terms of a series, we feel that this operation can be\ncontinued beyond all limit, and that there is, so to speak, no intrinsic\nreason for stopping.\n\nAs an abbreviation, let me call a mathematical continuum of the first\norder every aggregate of terms formed according to the same law as the\nscale of commensurable numbers. If we afterwards intercalate new steps\naccording to the law of formation of incommensurable numbers, we shall\nobtain what we will call a continuum of the second order.\n\n_Second Stage._--We have made hitherto only the first stride; we have\nexplained the origin of continua of the first order; but it is necessary\nto see why even they are not sufficient and why the incommensurable\nnumbers had to be invented.\n\nIf we try to imagine a line, it must have the characteristics of the\nphysical continuum, that is to say, we shall not be able to represent it\nexcept with a certain breadth. Two lines then will appear to us under\nthe form of two narrow bands, and, if we are content with this rough\nimage, it is evident that if the two lines cross they will have a common\npart.\n\nBut the pure geometer makes a further effort; without entirely\nrenouncing the aid of the senses, he tries to reach the concept of the\nline without breadth, of the point without extension. This he can only\nattain to by regarding the line as the limit toward which tends an ever\nnarrowing band, and the point as the limit toward which tends an ever\nlessening area. And then, our two bands, however narrow they may be,\nwill always have a common area, the smaller as they are the narrower,\nand whose limit will be what the pure geometer calls a point.\n\nThis is why it is said two lines which cross have a point in common, and\nthis truth seems intuitive.\n\nBut it would imply contradiction if lines were conceived as continua of\nthe first order, that is to say, if on the lines traced by the geometer\nshould be found only points having for coordinates rational numbers. The\ncontradiction would be manifest as soon as one affirmed, for example,\nthe existence of straights and circles.\n\nIt is clear, in fact, that if the points whose coordinates are\ncommensurable were alone regarded as real, the circle inscribed in a\nsquare and the diagonal of this square would not intersect, since the\ncoordinates of the point of intersection are incommensurable.\n\nThat would not yet be sufficient, because we should get in this way only\ncertain incommensurable numbers and not all those numbers.\n\nBut conceive of a straight line divided into two rays. Each of these\nrays will appear to our imagination as a band of a certain breadth;\nthese bands moreover will encroach one on the other, since there must be\nno interval between them. The common part will appear to us as a point\nwhich will always remain when we try to imagine our bands narrower and\nnarrower, so that we admit as an intuitive truth that if a straight is\ncut into two rays their common frontier is a point; we recognize here\nthe conception of Dedekind, in which an incommensurable number was\nregarded as the common frontier of two classes of rational numbers.\n\nSuch is the origin of the continuum of the second order, which is the\nmathematical continuum properly so called.\n\n_R\u00e9sum\u00e9._--In recapitulation, the mind has the faculty of creating\nsymbols, and it is thus that it has constructed the mathematical\ncontinuum, which is only a particular system of symbols. Its power is\nlimited only by the necessity of avoiding all contradiction; but the\nmind only makes use of this faculty if experience furnishes it a\nstimulus thereto.\n\nIn the case considered, this stimulus was the notion of the physical\ncontinuum, drawn from the rough data of the senses. But this notion\nleads to a series of contradictions from which it is necessary\nsuccessively to free ourselves. So we are forced to imagine a more and\nmore complicated system of symbols. That at which we stop is not only\nexempt from internal contradiction (it was so already at all the stages\nwe have traversed), but neither is it in contradiction with various\npropositions called intuitive, which are derived from empirical notions\nmore or less elaborated.\n\nMEASURABLE MAGNITUDE.--The magnitudes we have studied hitherto are not\n_measurable_; we can indeed say whether a given one of these magnitudes\nis greater than another, but not whether it is twice or thrice as great.\n\nSo far, I have only considered the order in which our terms are ranged.\nBut for most applications that does not suffice. We must learn to\ncompare the interval which separates any two terms. Only on this\ncondition does the continuum become a measurable magnitude and the\noperations of arithmetic applicable.\n\nThis can only be done by the aid of a new and special _convention_. We\nwill _agree_ that in such and such a case the interval comprised between\nthe terms _A_ and _B_ is equal to the interval which separates _C_ and\n_D_. For example, at the beginning of our work we have set out from the\nscale of the whole numbers and we have supposed intercalated between two\nconsecutive steps _n_ intermediary steps; well, these new steps will be\nby convention regarded as equidistant.\n\nThis is a way of defining the addition of two magnitudes, because if the\ninterval _AB_ is by definition equal to the interval _CD_, the interval\n_AD_ will be by definition the sum of the intervals _AB_ and _AC_.\n\nThis definition is arbitrary in a very large measure. It is not\ncompletely so, however. It is subjected to certain conditions and, for\nexample, to the rules of commutativity and associativity of addition.\nBut provided the definition chosen satisfies these rules, the choice is\nindifferent, and it is useless to particularize it.\n\nVARIOUS REMARKS.--We can now discuss several important questions:\n\n1\u00ba Is the creative power of the mind exhausted by the creation of the\nmathematical continuum?\n\nNo: the works of Du Bois-Reymond demonstrate it in a striking way.\n\nWe know that mathematicians distinguish between infinitesimals of\ndifferent orders and that those of the second order are infinitesimal,\nnot only in an absolute way, but also in relation to those of the first\norder. It is not difficult to imagine infinitesimals of fractional or\neven of irrational order, and thus we find again that scale of the\nmathematical continuum which has been dealt with in the preceding\npages.\n\nFurther, there are infinitesimals which are infinitely small in relation\nto those of the first order, and, on the contrary, infinitely great in\nrelation to those of order 1 + [epsilon], and that however small\n[epsilon] may be. Here, then, are new terms intercalated in our series,\nand if I may be permitted to revert to the phraseology lately employed\nwhich is very convenient though not consecrated by usage, I shall say\nthat thus has been created a sort of continuum of the third order.\n\nIt would be easy to go further, but that would be idle; one would only\nbe imagining symbols without possible application, and no one will think\nof doing that. The continuum of the third order, to which the\nconsideration of the different orders of infinitesimals leads, is itself\nnot useful enough to have won citizenship, and geometers regard it only\nas a mere curiosity. The mind uses its creative faculty only when\nexperience requires it.\n\n2\u00ba Once in possession of the concept of the mathematical continuum, is\none safe from contradictions analogous to those which gave birth to it?\n\nNo, and I will give an example.\n\nOne must be very wise not to regard it as evident that every curve has a\ntangent; and in fact if we picture this curve and a straight as two\nnarrow bands we can always so dispose them that they have a part in\ncommon without crossing. If we imagine then the breadth of these two\nbands to diminish indefinitely, this common part will always subsist\nand, at the limit, so to speak, the two lines will have a point in\ncommon without crossing, that is to say, they will be tangent.\n\nThe geometer who reasons in this way, consciously or not, is only doing\nwhat we have done above to prove two lines which cut have a point in\ncommon, and his intuition might seem just as legitimate.\n\nIt would deceive him however. We can demonstrate that there are curves\nwhich have no tangent, if such a curve is defined as an analytic\ncontinuum of the second order.\n\nWithout doubt some artifice analogous to those we have discussed above\nwould have sufficed to remove the contradiction; but, as this is met\nwith only in very exceptional cases, it has received no further\nattention.\n\nInstead of seeking to reconcile intuition with analysis, we have been\ncontent to sacrifice one of the two, and as analysis must remain\nimpeccable, we have decided against intuition.\n\nTHE PHYSICAL CONTINUUM OF SEVERAL DIMENSIONS.--We have discussed above\nthe physical continuum as derived from the immediate data of our senses,\nor, if you wish, from the rough results of Fechner's experiments; I have\nshown that these results are summed up in the contradictory formulas\n\n _A_ = _B_, _B_ = _C_, _A_ < _C_.\n\nLet us now see how this notion has been generalized and how from it has\ncome the concept of many-dimensional continua.\n\nConsider any two aggregates of sensations. Either we can discriminate\nthem one from another, or we can not, just as in Fechner's experiments a\nweight of 10 grams can be distinguished from a weight of 12 grams, but\nnot from a weight of 11 grams. This is all that is required to construct\nthe continuum of several dimensions.\n\nLet us call one of these aggregates of sensations an _element_. That\nwill be something analogous to the _point_ of the mathematicians; it\nwill not be altogether the same thing however. We can not say our\nelement is without extension, since we can not distinguish it from\nneighboring elements and it is thus surrounded by a sort of haze. If the\nastronomical comparison may be allowed, our 'elements' would be like\nnebulae, whereas the mathematical points would be like stars.\n\nThat being granted, a system of elements will form a _continuum_ if we\ncan pass from any one of them to any other, by a series of consecutive\nelements such that each is indistinguishable from the preceding. This\n_linear_ series is to the _line_ of the mathematician what an isolated\n_element_ was to the point.\n\nBefore going farther, I must explain what is meant by a _cut_. Consider\na continuum _C_ and remove from it certain of its elements which for an\ninstant we shall regard as no longer belonging to this continuum. The\naggregate of the elements so removed will be called a cut. It may happen\nthat, thanks to this cut, _C_ may be _subdivided_ into several distinct\ncontinua, the aggregate of the remaining elements ceasing to form a\nunique continuum.\n\nThere will then be on _C_ two elements, _A_ and _B_, that must be\nregarded as belonging to two distinct continua, and this will be\nrecognized because it will be impossible to find a linear series of\nconsecutive elements of _C_, each of these elements indistinguishable\nfrom the preceding, the first being _A_ and the last _B_, _without one\nof the elements of this series being indistinguishable from one of the\nelements of the cut_.\n\nOn the contrary, it may happen that the cut made is insufficient to\nsubdivide the continuum _C_. To classify the physical continua, we will\nexamine precisely what are the cuts which must be made to subdivide\nthem.\n\nIf a physical continuum _C_ can be subdivided by a cut reducing to a\nfinite number of elements all distinguishable from one another (and\nconsequently forming neither a continuum, nor several continua), we\nshall say _C_ is a _one-dimensional_ continuum.\n\nIf, on the contrary, _C_ can be subdivided only by cuts which are\nthemselves continua, we shall say _C_ has several dimensions. If cuts\nwhich are continua of one dimension suffice, we shall say _C_ has two\ndimensions; if cuts of two dimensions suffice, we shall say _C_ has\nthree dimensions, and so on.\n\nThus is defined the notion of the physical continuum of several\ndimensions, thanks to this very simple fact that two aggregates of\nsensations are distinguishable or indistinguishable.\n\nTHE MATHEMATICAL CONTINUUM OF SEVERAL DIMENSIONS.--Thence the notion of\nthe mathematical continuum of _n_ dimensions has sprung quite naturally\nby a process very like that we discussed at the beginning of this\nchapter. A point of such a continuum, you know, appears to us as defined\nby a system of _n_ distinct magnitudes called its coordinates.\n\nThese magnitudes need not always be measurable; there is, for instance,\na branch of geometry independent of the measurement of these magnitudes,\nin which it is only a question of knowing, for example, whether on a\ncurve _ABC_, the point _B_ is between the points _A_ and _C_, and not of\nknowing whether the arc _AB_ is equal to the arc _BC_ or twice as great.\nThis is what is called _Analysis Situs_.\n\nThis is a whole body of doctrine which has attracted the attention of\nthe greatest geometers and where we see flow one from another a series\nof remarkable theorems. What distinguishes these theorems from those of\nordinary geometry is that they are purely qualitative and that they\nwould remain true if the figures were copied by a draughtsman so awkward\nas to grossly distort the proportions and replace straights by strokes\nmore or less curved.\n\nThrough the wish to introduce measure next into the continuum just\ndefined this continuum becomes space, and geometry is born. But the\ndiscussion of this is reserved for Part Second.\n\n\n\n\nPART II\n\n\nSPACE\n\n\n\n\nCHAPTER III\n\nTHE NON-EUCLIDEAN GEOMETRIES\n\n\nEvery conclusion supposes premises; these premises themselves either are\nself-evident and need no demonstration, or can be established only by\nrelying upon other propositions, and since we can not go back thus to\ninfinity, every deductive science, and in particular geometry, must rest\non a certain number of undemonstrable axioms. All treatises on geometry\nbegin, therefore, by the enunciation of these axioms. But among these\nthere is a distinction to be made: Some, for example, 'Things which are\nequal to the same thing are equal to one another,' are not propositions\nof geometry, but propositions of analysis. I regard them as analytic\njudgments _a priori_, and shall not concern myself with them.\n\nBut I must lay stress upon other axioms which are peculiar to geometry.\nMost treatises enunciate three of these explicitly:\n\n1\u00ba Through two points can pass only one straight;\n\n2\u00ba The straight line is the shortest path from one point to another;\n\n3\u00ba Through a given point there is not more than one parallel to a given\nstraight.\n\nAlthough generally a proof of the second of these axioms is omitted, it\nwould be possible to deduce it from the other two and from those, much\nmore numerous, which are implicitly admitted without enunciating them,\nas I shall explain further on.\n\nIt was long sought in vain to demonstrate likewise the third axiom,\nknown as _Euclid's Postulate_. What vast effort has been wasted in this\nchimeric hope is truly unimaginable. Finally, in the first quarter of\nthe nineteenth century, and almost at the same time, a Hungarian and a\nRussian, Bolyai and Lobachevski, established irrefutably that this\ndemonstration is impossible; they have almost rid us of inventors of\ngeometries 'sans postulatum'; since then the Acad\u00e9mie des Sciences\nreceives only about one or two new demonstrations a year.\n\nThe question was not exhausted; it soon made a great stride by the\npublication of Riemann's celebrated memoir entitled: _Ueber die\nHypothesen welche der Geometrie zu Grunde liegen_. This paper has\ninspired most of the recent works of which I shall speak further on, and\namong which it is proper to cite those of Beltrami and of Helmholtz.\n\nTHE BOLYAI-LOBACHEVSKI GEOMETRY.--If it were possible to deduce Euclid's\npostulate from the other axioms, it is evident that in denying the\npostulate and admitting the other axioms, we should be led to\ncontradictory consequences; it would therefore be impossible to base on\nsuch premises a coherent geometry.\n\nNow this is precisely what Lobachevski did.\n\nHe assumes at the start that: _Through a given point can be drawn two\nparallels to a given straight_.\n\nAnd he retains besides all Euclid's other axioms. From these hypotheses\nhe deduces a series of theorems among which it is impossible to find any\ncontradiction, and he constructs a geometry whose faultless logic is\ninferior in nothing to that of the Euclidean geometry.\n\nThe theorems are, of course, very different from those to which we are\naccustomed, and they can not fail to be at first a little disconcerting.\n\nThus the sum of the angles of a triangle is always less than two right\nangles, and the difference between this sum and two right angles is\nproportional to the surface of the triangle.\n\nIt is impossible to construct a figure similar to a given figure but of\ndifferent dimensions.\n\nIf we divide a circumference into _n_ equal parts, and draw tangents at\nthe points of division, these _n_ tangents will form a polygon if the\nradius of the circle is small enough; but if this radius is sufficiently\ngreat they will not meet.\n\nIt is useless to multiply these examples; Lobachevski's propositions\nhave no relation to those of Euclid, but they are not less logically\nbound one to another.\n\nRIEMANN'S GEOMETRY.--Imagine a world uniquely peopled by beings of no\nthickness (height); and suppose these 'infinitely flat' animals are all\nin the same plane and can not get out. Admit besides that this world is\nsufficiently far from others to be free from their influence. While we\nare making hypotheses, it costs us no more to endow these beings with\nreason and believe them capable of creating a geometry. In that case,\nthey will certainly attribute to space only two dimensions.\n\nBut suppose now that these imaginary animals, while remaining without\nthickness, have the form of a spherical, and not of a plane, figure, and\nare all on the same sphere without power to get off. What geometry will\nthey construct? First it is clear they will attribute to space only two\ndimensions; what will play for them the r\u00f4le of the straight line will\nbe the shortest path from one point to another on the sphere, that is to\nsay, an arc of a great circle; in a word, their geometry will be the\nspherical geometry.\n\nWhat they will call space will be this sphere on which they must stay,\nand on which happen all the phenomena they can know. Their space will\ntherefore be _unbounded_ since on a sphere one can always go forward\nwithout ever being stopped, and yet it will be _finite_; one can never\nfind the end of it, but one can make a tour of it.\n\nWell, Riemann's geometry is spherical geometry extended to three\ndimensions. To construct it, the German mathematician had to throw\noverboard, not only Euclid's postulate, but also the first axiom: _Only\none straight can pass through two points_.\n\nOn a sphere, through two given points we can draw _in general_ only one\ngreat circle (which, as we have just seen, would play the r\u00f4le of the\nstraight for our imaginary beings); but there is an exception: if the\ntwo given points are diametrically opposite, an infinity of great\ncircles can be drawn through them.\n\nIn the same way, in Riemann's geometry (at least in one of its forms),\nthrough two points will pass in general only a single straight; but\nthere are exceptional cases where through two points an infinity of\nstraights can pass.\n\nThere is a sort of opposition between Riemann's geometry and that of\nLobachevski.\n\nThus the sum of the angles of a triangle is:\n\nEqual to two right angles in Euclid's geometry;\n\nLess than two right angles in that of Lobachevski;\n\nGreater than two right angles in that of Riemann.\n\nThe number of straights through a given point that can be drawn coplanar\nto a given straight, but nowhere meeting it, is equal:\n\nTo one in Euclid's geometry;\n\nTo zero in that of Riemann;\n\nTo infinity in that of Lobachevski.\n\nAdd that Riemann's space is finite, although unbounded, in the sense\ngiven above to these two words.\n\nTHE SURFACES OF CONSTANT CURVATURE.--One objection still remained\npossible. The theorems of Lobachevski and of Riemann present no\ncontradiction; but however numerous the consequences these two geometers\nhave drawn from their hypotheses, they must have stopped before\nexhausting them, since their number would be infinite; who can say then\nthat if they had pushed their deductions farther they would not have\neventually reached some contradiction?\n\nThis difficulty does not exist for Riemann's geometry, provided it is\nlimited to two dimensions; in fact, as we have seen, two-dimensional\nRiemannian geometry does not differ from spherical geometry, which is\nonly a branch of ordinary geometry, and consequently is beyond all\ndiscussion.\n\nBeltrami, in correlating likewise Lobachevski's two-dimensional geometry\nwith a branch of ordinary geometry, has equally refuted the objection so\nfar as it is concerned.\n\nHere is how he accomplished it. Consider any figure on a surface.\nImagine this figure traced on a flexible and inextensible canvas applied\nover this surface in such a way that when the canvas is displaced and\ndeformed, the various lines of this figure can change their form without\nchanging their length. In general, this flexible and inextensible figure\ncan not be displaced without leaving the surface; but there are certain\nparticular surfaces for which such a movement would be possible; these\nare the surfaces of constant curvature.\n\nIf we resume the comparison made above and imagine beings without\nthickness living on one of these surfaces, they will regard as possible\nthe motion of a figure all of whose lines remain constant in length. On\nthe contrary, such a movement would appear absurd to animals without\nthickness living on a surface of variable curvature.\n\nThese surfaces of constant curvature are of two sorts: Some are of\n_positive curvature_, and can be deformed so as to be applied over a\nsphere. The geometry of these surfaces reduces itself therefore to the\nspherical geometry, which is that of Riemann.\n\nThe others are of _negative curvature_. Beltrami has shown that the\ngeometry of these surfaces is none other than that of Lobachevski. The\ntwo-dimensional geometries of Riemann and Lobachevski are thus\ncorrelated to the Euclidean geometry.\n\nINTERPRETATION OF NON-EUCLIDEAN GEOMETRIES.--So vanishes the objection\nso far as two-dimensional geometries are concerned.\n\nIt would be easy to extend Beltrami's reasoning to three-dimensional\ngeometries. The minds that space of four dimensions does not repel will\nsee no difficulty in it, but they are few. I prefer therefore to proceed\notherwise.\n\nConsider a certain plane, which I shall call the fundamental plane, and\nconstruct a sort of dictionary, by making correspond each to each a\ndouble series of terms written in two columns, just as correspond in the\nordinary dictionaries the words of two languages whose significance is\nthe same:\n\n_Space_: Portion of space situated above the fundamental plane.\n\n_Plane_: Sphere cutting the fundamental plane orthogonally.\n\n_Straight_: Circle cutting the fundamental plane orthogonally.\n\n_Sphere_: Sphere.\n\n_Circle_: Circle.\n\n_Angle_: Angle.\n\n_Distance between two points_: Logarithm of the cross ratio of these two\npoints and the intersections of the fundamental plane with a circle\npassing through these two points and cutting it orthogonally. Etc.,\nEtc.\n\nNow take Lobachevski's theorems and translate them with the aid of this\ndictionary as we translate a German text with the aid of a\nGerman-English dictionary. _We shall thus obtain theorems of the\nordinary geometry._ For example, that theorem of Lobachevski: 'the sum\nof the angles of a triangle is less than two right angles' is translated\nthus: \"If a curvilinear triangle has for sides circle-arcs which\nprolonged would cut orthogonally the fundamental plane, the sum of the\nangles of this curvilinear triangle will be less than two right angles.\"\nThus, however far the consequences of Lobachevski's hypotheses are\npushed, they will never lead to a contradiction. In fact, if two of\nLobachevski's theorems were contradictory, it would be the same with the\ntranslations of these two theorems, made by the aid of our dictionary,\nbut these translations are theorems of ordinary geometry and no one\ndoubts that the ordinary geometry is free from contradiction. Whence\ncomes this certainty and is it justified? That is a question I can not\ntreat here because it would require to be enlarged upon, but which is\nvery interesting and I think not insoluble.\n\nNothing remains then of the objection above formulated. This is not all.\nLobachevski's geometry, susceptible of a concrete interpretation, ceases\nto be a vain logical exercise and is capable of applications; I have not\nthe time to speak here of these applications, nor of the aid that Klein\nand I have gotten from them for the integration of linear differential\nequations.\n\nThis interpretation moreover is not unique, and several dictionaries\nanalogous to the preceding could be constructed, which would enable us\nby a simple 'translation' to transform Lobachevski's theorems into\ntheorems of ordinary geometry.\n\nTHE IMPLICIT AXIOMS.--Are the axioms explicitly enunciated in our\ntreatises the sole foundations of geometry? We may be assured of the\ncontrary by noticing that after they are successively abandoned there\nare still left over some propositions common to the theories of Euclid,\nLobachevski and Riemann. These propositions must rest on premises the\ngeometers admit without enunciation. It is interesting to try to\ndisentangle them from the classic demonstrations.\n\nStuart Mill has claimed that every definition contains an axiom,\nbecause in defining one affirms implicitly the existence of the object\ndefined. This is going much too far; it is rare that in mathematics a\ndefinition is given without its being followed by the demonstration of\nthe existence of the object defined, and when this is dispensed with it\nis generally because the reader can easily supply it. It must not be\nforgotten that the word existence has not the same sense when it refers\nto a mathematical entity and when it is a question of a material object.\nA mathematical entity exists, provided its definition implies no\ncontradiction, either in itself, or with the propositions already\nadmitted.\n\nBut if Stuart Mill's observation can not be applied to all definitions,\nit is none the less just for some of them. The plane is sometimes\ndefined as follows:\n\nThe plane is a surface such that the straight which joins any two of its\npoints is wholly on this surface.\n\nThis definition manifestly hides a new axiom; it is true we might change\nit, and that would be preferable, but then we should have to enunciate\nthe axiom explicitly.\n\nOther definitions would suggest reflections not less important.\n\nSuch, for example, is that of the equality of two figures; two figures\nare equal when they can be superposed; to superpose them one must be\ndisplaced until it coincides with the other; but how shall it be\ndisplaced? If we should ask this, no doubt we should be told that it\nmust be done without altering the shape and as a rigid solid. The\nvicious circle would then be evident.\n\nIn fact this definition defines nothing; it would have no meaning for a\nbeing living in a world where there were only fluids. If it seems clear\nto us, that is because we are used to the properties of natural solids\nwhich do not differ much from those of the ideal solids, all of whose\ndimensions are invariable.\n\nYet, imperfect as it may be, this definition implies an axiom.\n\nThe possibility of the motion of a rigid figure is not a self-evident\ntruth, or at least it is so only in the fashion of Euclid's postulate\nand not as an analytic judgment _a priori_ would be.\n\nMoreover, in studying the definitions and the demonstrations of\ngeometry, we see that one is obliged to admit without proof not only the\npossibility of this motion, but some of its properties besides.\n\nThis is at once seen from the definition of the straight line. Many\ndefective definitions have been given, but the true one is that which is\nimplied in all the demonstrations where the straight line enters:\n\n\"It may happen that the motion of a rigid figure is such that all the\npoints of a line belonging to this figure remain motionless while all\nthe points situated outside of this line move. Such a line will be\ncalled a straight line.\" We have designedly, in this enunciation,\nseparated the definition from the axiom it implies.\n\nMany demonstrations, such as those of the cases of the equality of\ntriangles, of the possibility of dropping a perpendicular from a point\nto a straight, presume propositions which are not enunciated, for they\nrequire the admission that it is possible to transport a figure in a\ncertain way in space.\n\nTHE FOURTH GEOMETRY.--Among these implicit axioms, there is one which\nseems to me to merit some attention, because when it is abandoned a\nfourth geometry can be constructed as coherent as those of Euclid,\nLobachevski and Riemann.\n\nTo prove that a perpendicular may always be erected at a point _A_ to a\nstraight _AB_, we consider a straight _AC_ movable around the point _A_\nand initially coincident with the fixed straight _AB_; and we make it\nturn about the point _A_ until it comes into the prolongation of _AB_.\n\nThus two propositions are presupposed: First, that such a rotation is\npossible, and next that it may be continued until the two straights come\ninto the prolongation one of the other.\n\nIf the first point is admitted and the second rejected, we are led to a\nseries of theorems even stranger than those of Lobachevski and Riemann,\nbut equally exempt from contradiction.\n\nI shall cite only one of these theorems and that not the most singular:\n_A real straight may be perpendicular to itself_.\n\nLIE'S THEOREM.--The number of axioms implicitly introduced in the\nclassic demonstrations is greater than necessary, and it would be\ninteresting to reduce it to a minimum. It may first be asked whether\nthis reduction is possible, whether the number of necessary axioms and\nthat of imaginable geometries are not infinite.\n\nA theorem of Sophus Lie dominates this whole discussion. It may be thus\nenunciated:\n\nSuppose the following premises are admitted:\n\n1\u00ba Space has _n_ dimensions;\n\n2\u00ba The motion of a rigid figure is possible;\n\n3\u00ba It requires _p_ conditions to determine the position of this figure\nin space.\n\n_The number of geometries compatible with these premises will be\nlimited._\n\nI may even add that if _n_ is given, a superior limit can be assigned to\n_p_.\n\nIf therefore the possibility of motion is admitted, there can be\ninvented only a finite (and even a rather small) number of\nthree-dimensional geometries.\n\nRIEMANN'S GEOMETRIES.--Yet this result seems contradicted by Riemann,\nfor this savant constructs an infinity of different geometries, and that\nto which his name is ordinarily given is only a particular case.\n\nAll depends, he says, on how the length of a curve is defined. Now,\nthere is an infinity of ways of defining this length, and each of them\nmay be the starting point of a new geometry.\n\nThat is perfectly true, but most of these definitions are incompatible\nwith the motion of a rigid figure, which in the theorem of Lie is\nsupposed possible. These geometries of Riemann, in many ways so\ninteresting, could never therefore be other than purely analytic and\nwould not lend themselves to demonstrations analogous to those of\nEuclid.\n\nON THE NATURE OF AXIOMS.--Most mathematicians regard Lobachevski's\ngeometry only as a mere logical curiosity; some of them, however, have\ngone farther. Since several geometries are possible, is it certain ours\nis the true one? Experience no doubt teaches us that the sum of the\nangles of a triangle is equal to two right angles; but this is because\nthe triangles we deal with are too little; the difference, according to\nLobachevski, is proportional to the surface of the triangle; will it not\nperhaps become sensible when we shall operate on larger triangles or\nwhen our measurements shall become more precise? The Euclidean geometry\nwould thus be only a provisional geometry.\n\nTo discuss this opinion, we should first ask ourselves what is the\nnature of the geometric axioms.\n\nAre they synthetic _a priori_ judgments, as Kant said?\n\nThey would then impose themselves upon us with such force that we could\nnot conceive the contrary proposition, nor build upon it a theoretic\nedifice. There would be no non-Euclidean geometry.\n\nTo be convinced of it take a veritable synthetic _a priori_ judgment,\nthe following, for instance, of which we have seen the preponderant r\u00f4le\nin the first chapter:\n\n_If a theorem is true for the number 1, and if it has been proved that\nit is true of n + 1 provided it is true of n, it will be true of all the\npositive whole numbers._\n\nThen try to escape from that and, denying this proposition, try to found\na false arithmetic analogous to non-Euclidean geometry--it can not be\ndone; one would even be tempted at first blush to regard these judgments\nas analytic.\n\nMoreover, resuming our fiction of animals without thickness, we can\nhardly admit that these beings, if their minds are like ours, would\nadopt the Euclidean geometry which would be contradicted by all their\nexperience.\n\nShould we therefore conclude that the axioms of geometry are\nexperimental verities? But we do not experiment on ideal straights or\ncircles; it can only be done on material objects. On what then could be\nbased experiments which should serve as foundation for geometry? The\nanswer is easy.\n\nWe have seen above that we constantly reason as if the geometric figures\nbehaved like solids. What geometry would borrow from experience would\ntherefore be the properties of these bodies. The properties of light and\nits rectilinear propagation have also given rise to some of the\npropositions of geometry, and in particular those of projective\ngeometry, so that from this point of view one would be tempted to say\nthat metric geometry is the study of solids, and projective, that of\nlight.\n\nBut a difficulty remains, and it is insurmountable. If geometry were an\nexperimental science, it would not be an exact science, it would be\nsubject to a continual revision. Nay, it would from this very day be\nconvicted of error, since we know that there is no rigorously rigid\nsolid.\n\nThe _axioms of geometry therefore are neither synthetic_ a priori\n_judgments nor experimental facts_.\n\nThey are _conventions_; our choice among all possible conventions is\n_guided_ by experimental facts; but it remains _free_ and is limited\nonly by the necessity of avoiding all contradiction. Thus it is that the\npostulates can remain _rigorously_ true even though the experimental\nlaws which have determined their adoption are only approximative.\n\nIn other words, _the axioms of geometry_ (I do not speak of those of\narithmetic) _are merely disguised definitions_.\n\nThen what are we to think of that question: Is the Euclidean geometry\ntrue?\n\nIt has no meaning.\n\nAs well ask whether the metric system is true and the old measures\nfalse; whether Cartesian coordinates are true and polar coordinates\nfalse. One geometry can not be more true than another; it can only be\n_more convenient_.\n\nNow, Euclidean geometry is, and will remain, the most convenient:\n\n1\u00ba Because it is the simplest; and it is so not only in consequence of\nour mental habits, or of I know not what direct intuition that we may\nhave of Euclidean space; it is the simplest in itself, just as a\npolynomial of the first degree is simpler than one of the second; the\nformulas of spherical trigonometry are more complicated than those of\nplane trigonometry, and they would still appear so to an analyst\nignorant of their geometric signification.\n\n2\u00ba Because it accords sufficiently well with the properties of natural\nsolids, those bodies which our hands and our eyes compare and with which\nwe make our instruments of measure.\n\n\n\n\nCHAPTER IV\n\nSPACE AND GEOMETRY\n\n\nLet us begin by a little paradox.\n\nBeings with minds like ours, and having the same senses as we, but\nwithout previous education, would receive from a suitably chosen\nexternal world impressions such that they would be led to construct a\ngeometry other than that of Euclid and to localize the phenomena of that\nexternal world in a non-Euclidean space, or even in a space of four\ndimensions.\n\nAs for us, whose education has been accomplished by our actual world, if\nwe were suddenly transported into this new world, we should have no\ndifficulty in referring its phenomena to our Euclidean space.\nConversely, if these beings were transported into our environment, they\nwould be led to relate our phenomena to non-Euclidean space.\n\nNay more; with a little effort we likewise could do it. A person who\nshould devote his existence to it might perhaps attain to a realization\nof the fourth dimension.\n\nGEOMETRIC SPACE AND PERCEPTUAL SPACE.--It is often said the images of\nexternal objects are localized in space, even that they can not be\nformed except on this condition. It is also said that this space, which\nserves thus as a ready prepared _frame_ for our sensations and our\nrepresentations, is identical with that of the geometers, of which it\npossesses all the properties.\n\nTo all the good minds who think thus, the preceding statement must have\nappeared quite extraordinary. But let us see whether they are not\nsubject to an illusion that a more profound analysis would dissipate.\n\nWhat, first of all, are the properties of space, properly so called? I\nmean of that space which is the object of geometry and which I shall\ncall _geometric space_.\n\nThe following are some of the most essential:\n\n1\u00ba It is continuous;\n\n2\u00ba It is infinite;\n\n3\u00ba It has three dimensions;\n\n4\u00ba It is homogeneous, that is to say, all its points are identical one\nwith another;\n\n5\u00ba It is isotropic, that is to say, all the straights which pass through\nthe same point are identical one with another.\n\nCompare it now to the frame of our representations and our sensations,\nwhich I may call _perceptual space_.\n\nVISUAL SPACE.--Consider first a purely visual impression, due to an\nimage formed on the bottom of the retina.\n\nA cursory analysis shows us this image as continuous, but as possessing\nonly two dimensions; this already distinguishes from geometric space\nwhat we may call _pure visual space_.\n\nBesides, this image is enclosed in a limited frame.\n\nFinally, there is another difference not less important: _this pure\nvisual space is not homogeneous_. All the points of the retina, aside\nfrom the images which may there be formed, do not play the same r\u00f4le.\nThe yellow spot can in no way be regarded as identical with a point on\nthe border of the retina. In fact, not only does the same object produce\nthere much more vivid impressions, but in every _limited_ frame the\npoint occupying the center of the frame will never appear as equivalent\nto a point near one of the borders.\n\nNo doubt a more profound analysis would show us that this continuity of\nvisual space and its two dimensions are only an illusion; it would\nseparate it therefore still more from geometric space, but we shall not\ndwell on this remark.\n\nSight, however, enables us to judge of distances and consequently to\nperceive a third dimension. But every one knows that this perception of\nthe third dimension reduces itself to the sensation of the effort at\naccommodation it is necessary to make, and to that of the convergence\nwhich must be given to the two eyes, to perceive an object distinctly.\n\nThese are muscular sensations altogether different from the visual\nsensations which have given us the notion of the first two dimensions.\nThe third dimension therefore will not appear to us as playing the same\nr\u00f4le as the other two. What may be called _complete visual space_ is\ntherefore not an isotropic space.\n\nIt has, it is true, precisely three dimensions, which means that the\nelements of our visual sensations (those at least which combine to form\nthe notion of extension) will be completely defined when three of them\nare known; to use the language of mathematics, they will be functions of\nthree independent variables.\n\nBut examine the matter a little more closely. The third dimension is\nrevealed to us in two different ways: by the effort of accommodation and\nby the convergence of the eyes.\n\nNo doubt these two indications are always concordant, there is a\nconstant relation between them, or, in mathematical terms, the two\nvariables which measure these two muscular sensations do not appear to\nus as independent; or again, to avoid an appeal to mathematical notions\nalready rather refined, we may go back to the language of the preceding\nchapter and enunciate the same fact as follows: If two sensations of\nconvergence, _A_ and _B_, are indistinguishable, the two sensations of\naccommodation, _A'_ and _B'_, which respectively accompany them, will be\nequally indistinguishable.\n\nBut here we have, so to speak, an experimental fact; _a priori_ nothing\nprevents our supposing the contrary, and if the contrary takes place, if\nthese two muscular sensations vary independently of one another, we\nshall have to take account of one more independent variable, and\n'complete visual space' will appear to us as a physical continuum of\nfour dimensions.\n\nWe have here even, I will add, a fact of _external_ experience. Nothing\nprevents our supposing that a being with a mind like ours, having the\nsame sense organs that we have, may be placed in a world where light\nwould only reach him after having traversed reflecting media of\ncomplicated form. The two indications which serve us in judging\ndistances would cease to be connected by a constant relation. A being\nwho should achieve in such a world the education of his senses would no\ndoubt attribute four dimensions to complete visual space.\n\nTACTILE SPACE AND MOTOR SPACE.--'Tactile space' is still more\ncomplicated than visual space and farther removed from geometric space.\nIt is superfluous to repeat for touch the discussion I have given for\nsight.\n\nBut apart from the data of sight and touch, there are other sensations\nwhich contribute as much and more than they to the genesis of the notion\nof space. These are known to every one; they accompany all our\nmovements, and are usually called muscular sensations.\n\nThe corresponding frame constitutes what may be called _motor space_.\n\nEach muscle gives rise to a special sensation capable of augmenting or\nof diminishing, so that the totality of our muscular sensations will\ndepend upon as many variables as we have muscles. From this point of\nview, _motor space would have as many dimensions as we have muscles_.\n\nI know it will be said that if the muscular sensations contribute to\nform the notion of space, it is because we have the sense of the\n_direction_ of each movement and that it makes an integrant part of the\nsensation. If this were so, if a muscular sensation could not arise\nexcept accompanied by this geometric sense of direction, geometric space\nwould indeed be a form imposed upon our sensibility.\n\nBut I perceive nothing at all of this when I analyze my sensations.\n\nWhat I do see is that the sensations which correspond to movements in\nthe same direction are connected in my mind by a mere _association of\nideas_. It is to this association that what we call 'the sense of\ndirection' is reducible. This feeling therefore can not be found in a\nsingle sensation.\n\nThis association is extremely complex, for the contraction of the same\nmuscle may correspond, according to the position of the limbs, to\nmovements of very different direction.\n\nBesides, it is evidently acquired; it is, like all associations of\nideas, the result of a _habit_; this habit itself results from very\nnumerous _experiences_; without any doubt, if the education of our\nsenses had been accomplished in a different environment, where we should\nhave been subjected to different impressions, contrary habits would have\narisen and our muscular sensations would have been associated according\nto other laws.\n\nCHARACTERISTICS OF PERCEPTUAL SPACE.--Thus perceptual space, under its\ntriple form, visual, tactile and motor, is essentially different from\ngeometric space.\n\nIt is neither homogeneous, nor isotropic; one can not even say that it\nhas three dimensions.\n\nIt is often said that we 'project' into geometric space the objects of\nour external perception; that we 'localize' them.\n\nHas this a meaning, and if so what?\n\nDoes it mean that we _represent_ to ourselves external objects in\ngeometric space?\n\nOur representations are only the reproduction of our sensations; they\ncan therefore be ranged only in the same frame as these, that is to say,\nin perceptual space.\n\nIt is as impossible for us to represent to ourselves external bodies in\ngeometric space, as it is for a painter to paint on a plane canvas\nobjects with their three dimensions.\n\nPerceptual space is only an image of geometric space, an image altered\nin shape by a sort of perspective, and we can represent to ourselves\nobjects only by bringing them under the laws of this perspective.\n\nTherefore we do not _represent_ to ourselves external bodies in\ngeometric space, but we _reason_ on these bodies as if they were\nsituated in geometric space.\n\nWhen it is said then that we 'localize' such and such an object at such\nand such a point of space, what does it mean?\n\n_It simply means that we represent to ourselves the movements it would\nbe necessary to make to reach that object_; and one may not say that to\nrepresent to oneself these movements, it is necessary to project the\nmovements themselves in space and that the notion of space must,\nconsequently, pre-exist.\n\nWhen I say that we represent to ourselves these movements, I mean only\nthat we represent to ourselves the muscular sensations which accompany\nthem and which have no geometric character whatever, which consequently\ndo not at all imply the preexistence of the notion of space.\n\nCHANGE OF STATE AND CHANGE OF POSITION.--But, it will be said, if the\nidea of geometric space is not imposed upon our mind, and if, on the\nother hand, none of our sensations can furnish it, how could it have\ncome into existence?\n\nThis is what we have now to examine, and it will take some time, but I\ncan summarize in a few words the attempt at explanation that I am about\nto develop.\n\n_None of our sensations, isolated, could have conducted us to the idea\nof space; we are led to it only in studying the laws, according to which\nthese sensations succeed each other._\n\nWe see first that our impressions are subject to change; but among the\nchanges we ascertain we are soon led to make a distinction.\n\nAt one time we say that the objects which cause these impressions have\nchanged state, at another time that they have changed position, that\nthey have only been displaced.\n\nWhether an object changes its state or merely its position, this is\nalways translated for us in the same manner: _by a modification in an\naggregate of impressions_.\n\nHow then could we have been led to distinguish between the two? It is\neasy to account for. If there has only been a change of position, we can\nrestore the primitive aggregate of impressions by making movements which\nreplace us opposite the mobile object in the same _relative_ situation.\nWe thus _correct_ the modification that happened and we reestablish the\ninitial state by an inverse modification.\n\nIf it is a question of sight, for example, and if an object changes its\nplace before our eye, we can 'follow it with the eye' and maintain its\nimage on the same point of the retina by appropriate movements of the\neyeball.\n\nThese movements we are conscious of because they are voluntary and\nbecause they are accompanied by muscular sensations, but that does not\nmean that we represent them to ourselves in geometric space.\n\nSo what characterizes change of position, what distinguishes it from\nchange of state, is that it can always be corrected in this way.\n\nIt may therefore happen that we pass from the totality of impressions\n_A_ to the totality _B_ in two different ways:\n\n1\u00ba Involuntarily and without experiencing muscular sensations; this\nhappens when it is the object which changes place;\n\n2\u00b0 Voluntarily and with muscular sensations; this happens when the\nobject is motionless, but we move so that the object has relative motion\nwith reference to us.\n\nIf this be so, the passage from the totality _A_ to the totality _B_ is\nonly a change of position.\n\nIt follows from this that sight and touch could not have given us the\nnotion of space without the aid of the 'muscular sense.'\n\nNot only could this notion not be derived from a single sensation or\neven _from a series of sensations_, but what is more, an _immobile_\nbeing could never have acquired it, since, not being able to _correct_\nby his movements the effects of the changes of position of exterior\nobjects, he would have had no reason whatever to distinguish them from\nchanges of state. Just as little could he have acquired it if his\nmotions had not been voluntary or were unaccompanied by any sensations.\n\nCONDITIONS OF COMPENSATION.--How is a like compensation possible, of\nsuch sort that two changes, otherwise independent of each other,\nreciprocally correct each other?\n\nA mind already familiar with geometry would reason as follows:\nEvidently, if there is to be compensation, the various parts of the\nexternal object, on the one hand, and the various sense organs, on the\nother hand, must be in the same _relative_ position after the double\nchange. And, for that to be the case, the various parts of the external\nobject must likewise have retained in reference to each other the same\nrelative position, and the same must be true of the various parts of our\nbody in regard to each other.\n\nIn other words, the external object, in the first change, must be\ndisplaced as is a rigid solid, and so must it be with the whole of our\nbody in the second change which corrects the first.\n\nUnder these conditions, compensation may take place.\n\nBut we who as yet know nothing of geometry, since for us the notion of\nspace is not yet formed, we can not reason thus, we can not foresee _a\npriori_ whether compensation is possible. But experience teaches us that\nit sometimes happens, and it is from this experimental fact that we\nstart to distinguish changes of state from changes of position.\n\nSOLID BODIES AND GEOMETRY.--Among surrounding objects there are some\nwhich frequently undergo displacements susceptible of being thus\ncorrected by a correlative movement of our own body; these are the\n_solid bodies_. The other objects, whose form is variable, only\nexceptionally undergo like displacements (change of position without\nchange of form). When a body changes its place _and its shape_, we can\nno longer, by appropriate movements, bring back our sense-organs into\nthe same _relative_ situation with regard to this body; consequently we\ncan no longer reestablish the primitive totality of impressions.\n\nIt is only later, and as a consequence of new experiences, that we learn\nhow to decompose the bodies of variable form into smaller elements, such\nthat each is displaced almost in accordance with the same laws as solid\nbodies. Thus we distinguish 'deformations' from other changes of state;\nin these deformations, each element undergoes a mere change of position,\nwhich can be corrected, but the modification undergone by the aggregate\nis more profound and is no longer susceptible of correction by a\ncorrelative movement.\n\nSuch a notion is already very complex and must have been relatively late\nin appearing; moreover it could not have arisen if the observation of\nsolid bodies had not already taught us to distinguish changes of\nposition.\n\n_Therefore, if there were no solid bodies in nature, there would be no\ngeometry._\n\nAnother remark also deserves a moment's attention. Suppose a solid body\nto occupy successively the positions [alpha] and [beta]; in its first\nposition, it will produce on us the totality of impressions _A_, and in\nits second position the totality of impressions _B_. Let there be now a\nsecond solid body, having qualities entirely different from the first,\nfor example, a different color. Suppose it to pass from the position\n[alpha], where it gives us the totality of impressions _A'_, to the\nposition [beta], where it gives the totality of impressions _B'_.\n\nIn general, the totality _A_ will have nothing in common with the\ntotality _A'_, nor the totality _B_ with the totality _B'_. The\ntransition from the totality _A_ to the totality _B_ and that from the\ntotality _A'_ to the totality _B'_ are therefore two changes which _in\nthemselves_ have in general nothing in common.\n\nAnd yet we regard these two changes both as displacements and,\nfurthermore, we consider them as the _same_ displacement. How can that\nbe?\n\nIt is simply because they can both be corrected by the _same_\ncorrelative movement of our body.\n\n'Correlative movement' therefore constitutes the _sole connection_\nbetween two phenomena which otherwise we never should have dreamt of\nlikening.\n\nOn the other hand, our body, thanks to the number of its articulations\nand muscles, may make a multitude of different movements; but all are\nnot capable of 'correcting' a modification of external objects; only\nthose will be capable of it in which our whole body, or at least all\nthose of our sense-organs which come into play, are displaced as a\nwhole, that is, without their relative positions varying, or in the\nfashion of a solid body.\n\nTo summarize:\n\n1\u00ba We are led at first to distinguish two categories of phenomena:\n\nSome, involuntary, unaccompanied by muscular sensations, are attributed\nby us to external objects; these are external changes;\n\nOthers, opposite in character and attributed by us to the movements of\nour own body, are internal changes;\n\n2\u00ba We notice that certain changes of each of these categories may be\ncorrected by a correlative change of the other category;\n\n3\u00ba We distinguish among external changes those which have thus a\ncorrelative in the other category; these we call displacements; and just\nso among the internal changes, we distinguish those which have a\ncorrelative in the first category.\n\nThus are defined, thanks to this reciprocity, a particular class of\nphenomena which we call displacements.\n\n_The laws of these phenomena constitute the object of geometry._\n\nLAW OF HOMOGENEITY.--The first of these laws is the law of homogeneity.\n\nSuppose that, by an external change [alpha], we pass from the totality\nof impressions _A_ to the totality _B_, then that this change [alpha] is\ncorrected by a correlative voluntary movement [beta], so that we are\nbrought back to the totality _A_.\n\nSuppose now that another external change [alpha]' makes us pass anew\nfrom the totality _A_ to the totality _B_.\n\nExperience teaches us that this change [alpha]' is, like [alpha],\nsusceptible of being corrected by a correlative voluntary movement\n[beta]' and that this movement [beta]' corresponds to the same muscular\nsensations as the movement [beta] which corrected [alpha].\n\nThis fact is usually enunciated by saying that _space is homogeneous and\nisotropic_.\n\nIt may also be said that a movement which has once been produced may be\nrepeated a second and a third time, and so on, without its properties\nvarying.\n\nIn the first chapter, where we discussed the nature of mathematical\nreasoning, we saw the importance which must be attributed to the\npossibility of repeating indefinitely the same operation.\n\nIt is from this repetition that mathematical reasoning gets its power;\nit is, therefore, thanks to the law of homogeneity, that it has a hold\non the geometric facts.\n\nFor completeness, to the law of homogeneity should be added a multitude\nof other analogous laws, into the details of which I do not wish to\nenter, but which mathematicians sum up in a word by saying that\ndisplacements form 'a group.'\n\nTHE NON-EUCLIDEAN WORLD.--If geometric space were a frame imposed on\n_each_ of our representations, considered individually, it would be\nimpossible to represent to ourselves an image stripped of this frame,\nand we could change nothing of our geometry.\n\nBut this is not the case; geometry is only the r\u00e9sum\u00e9 of the laws\naccording to which these images succeed each other. Nothing then\nprevents us from imagining a series of representations, similar in all\npoints to our ordinary representations, but succeeding one another\naccording to laws different from those to which we are accustomed.\n\nWe can conceive then that beings who received their education in an\nenvironment where these laws were thus upset might have a geometry very\ndifferent from ours.\n\nSuppose, for example, a world enclosed in a great sphere and subject to\nthe following laws:\n\nThe temperature is not uniform; it is greatest at the center, and\ndiminishes in proportion to the distance from the center, to sink to\nabsolute zero when the sphere is reached in which this world is\nenclosed.\n\nTo specify still more precisely the law in accordance with which this\ntemperature varies: Let _R_ be the radius of the limiting sphere;\nlet _r_ be the distance of the point considered from the center\nof this sphere. The absolute temperature shall be proportional\nto _R_^{2} - _r_^{2}.\n\nI shall further suppose that, in this world, all bodies have the same\ncoefficient of dilatation, so that the length of any rule is\nproportional to its absolute temperature.\n\nFinally, I shall suppose that a body transported from one point to\nanother of different temperature is put immediately into thermal\nequilibrium with its new environment.\n\nNothing in these hypotheses is contradictory or unimaginable.\n\nA movable object will then become smaller and smaller in proportion as\nit approaches the limit-sphere.\n\nNote first that, though this world is limited from the point of view of\nour ordinary geometry, it will appear infinite to its inhabitants.\n\nIn fact, when these try to approach the limit-sphere, they cool off and\nbecome smaller and smaller. Therefore the steps they take are also\nsmaller and smaller, so that they can never reach the limiting sphere.\n\nIf, for us, geometry is only the study of the laws according to which\nrigid solids move, for these imaginary beings it will be the study of\nthe laws of motion of solids _distorted by the differences of\ntemperature_ just spoken of.\n\nNo doubt, in our world, natural solids likewise undergo variations of\nform and volume due to warming or cooling. But we neglect these\nvariations in laying the foundations of geometry, because, besides their\nbeing very slight, they are irregular and consequently seem to us\naccidental.\n\nIn our hypothetical world, this would no longer be the case, and these\nvariations would follow regular and very simple laws.\n\nMoreover, the various solid pieces of which the bodies of its\ninhabitants would be composed would undergo the same variations of form\nand volume.\n\nI will make still another hypothesis; I will suppose light traverses\nmedia diversely refractive and such that the index of refraction is\ninversely proportional to _R_^{2} - _r_^{2}. It is easy to see that,\nunder these conditions, the rays of light would not be rectilinear, but\ncircular.\n\nTo justify what precedes, it remains for me to show that certain changes\nin the position of external objects can be _corrected_ by correlative\nmovements of the sentient beings inhabiting this imaginary world, and\nthat in such a way as to restore the primitive aggregate of impressions\nexperienced by these sentient beings.\n\nSuppose in fact that an object is displaced, undergoing deformation, not\nas a rigid solid, but as a solid subjected to unequal dilatations in\nexact conformity to the law of temperature above supposed. Permit me for\nbrevity to call such a movement a _non-Euclidean displacement_.\n\nIf a sentient being happens to be in the neighborhood, his impressions\nwill be modified by the displacement of the object, but he can\nreestablish them by moving in a suitable manner. It suffices if finally\nthe aggregate of the object and the sentient being, considered as\nforming a single body, has undergone one of those particular\ndisplacements I have just called non-Euclidean. This is possible if it\nbe supposed that the limbs of these beings dilate according to the same\nlaw as the other bodies of the world they inhabit.\n\nAlthough from the point of view of our ordinary geometry there is a\ndeformation of the bodies in this displacement and their various parts\nare no longer in the same relative position, nevertheless we shall see\nthat the impressions of the sentient being have once more become the\nsame.\n\nIn fact, though the mutual distances of the various parts may have\nvaried, yet the parts originally in contact are again in contact.\nTherefore the tactile impressions have not changed.\n\nOn the other hand, taking into account the hypothesis made above in\nregard to the refraction and the curvature of the rays of light, the\nvisual impressions will also have remained the same.\n\nThese imaginary beings will therefore like ourselves be led to classify\nthe phenomena they witness and to distinguish among them the 'changes of\nposition' susceptible of correction by a correlative voluntary movement.\n\nIf they construct a geometry, it will not be, as ours is, the study of\nthe movements of our rigid solids; it will be the study of the changes\nof position which they will thus have distinguished and which are none\nother than the 'non-Euclidean displacements'; _it will be non-Euclidean\ngeometry_.\n\nThus beings like ourselves, educated in such a world, would not have the\nsame geometry as ours.\n\nTHE WORLD OF FOUR DIMENSIONS.--We can represent to ourselves a\nfour-dimensional world just as well as a non-Euclidean.\n\nThe sense of sight, even with a single eye, together with the muscular\nsensations relative to the movements of the eyeball, would suffice to\nteach us space of three dimensions.\n\nThe images of external objects are painted on the retina, which is a\ntwo-dimensional canvas; they are _perspectives_.\n\nBut, as eye and objects are movable, we see in succession various\nperspectives of the same body, taken from different points of view.\n\nAt the same time, we find that the transition from one perspective to\nanother is often accompanied by muscular sensations.\n\nIf the transition from the perspective _A_ to the perspective _B_, and\nthat from the perspective _A'_ to the perspective _B'_ are accompanied\nby the same muscular sensations, we liken them one to the other as\noperations of the same nature.\n\nStudying then the laws according to which these operations combine, we\nrecognize that they form a group, which has the same structure as that\nof the movements of rigid solids.\n\nNow, we have seen that it is from the properties of this group we have\nderived the notion of geometric space and that of three dimensions.\n\nWe understand thus how the idea of a space of three dimensions could\ntake birth from the pageant of these perspectives, though each of them\nis of only two dimensions, since _they follow one another according to\ncertain laws_.\n\nWell, just as the perspective of a three-dimensional figure can be made\non a plane, we can make that of a four-dimensional figure on a picture\nof three (or of two) dimensions. To a geometer this is only child's\nplay.\n\nWe can even take of the same figure several perspectives from several\ndifferent points of view.\n\nWe can easily represent to ourselves these perspectives, since they are\nof only three dimensions.\n\nImagine that the various perspectives of the same object succeed one\nanother, and that the transition from one to the other is accompanied by\nmuscular sensations.\n\nWe shall of course consider two of these transitions as two operations\nof the same nature when they are associated with the same muscular\nsensations.\n\nNothing then prevents us from imagining that these operations combine\naccording to any law we choose, for example, so as to form a group with\nthe same structure as that of the movements of a rigid solid of four\ndimensions.\n\nHere there is nothing unpicturable, and yet these sensations are\nprecisely those which would be felt by a being possessed of a\ntwo-dimensional retina who could move in space of four dimensions. In\nthis sense we may say the fourth dimension is imaginable.\n\nCONCLUSIONS.--We see that experience plays an indispensable r\u00f4le in the\ngenesis of geometry; but it would be an error thence to conclude that\ngeometry is, even in part, an experimental science.\n\nIf it were experimental, it would be only approximative and provisional.\nAnd what rough approximation!\n\nGeometry would be only the study of the movements of solids; but in\nreality it is not occupied with natural solids, it has for object\ncertain ideal solids, absolutely rigid, which are only a simplified and\nvery remote image of natural solids.\n\nThe notion of these ideal solids is drawn from all parts of our mind,\nand experience is only an occasion which induces us to bring it forth\nfrom them.\n\nThe object of geometry is the study of a particular 'group'; but the\ngeneral group concept pre-exists, at least potentially, in our minds. It\nis imposed on us, not as form of our sense, but as form of our\nunderstanding.\n\nOnly, from among all the possible groups, that must be chosen which will\nbe, so to speak, the _standard_ to which we shall refer natural\nphenomena.\n\nExperience guides us in this choice without forcing it upon us; it\ntells us not which is the truest geometry, but which is the most\n_convenient_.\n\nNotice that I have been able to describe the fantastic worlds above\nimagined _without ceasing to employ the language of ordinary geometry_.\n\nAnd, in fact, we should not have to change it if transported thither.\n\nBeings educated there would doubtless find it more convenient to create\na geometry different from ours, and better adapted to their impressions.\nAs for us, in face of the _same_ impressions, it is certain we should\nfind it more convenient not to change our habits.\n\n\n\n\nCHAPTER V\n\nEXPERIENCE AND GEOMETRY\n\n\n1. Already in the preceding pages I have several times tried to show\nthat the principles of geometry are not experimental facts and that in\nparticular Euclid's postulate can not be proven experimentally.\n\nHowever decisive appear to me the reasons already given, I believe I\nshould emphasize this point because here a false idea is profoundly\nrooted in many minds.\n\n2. If we construct a material circle, measure its radius and\ncircumference, and see if the ratio of these two lengths is equal to\n[pi], what shall we have done? We shall have made an experiment on the\nproperties of the matter with which we constructed this _round thing_,\nand of that of which the measure used was made.\n\n3. GEOMETRY AND ASTRONOMY.--The question has also been put in another\nway. If Lobachevski's geometry is true, the parallax of a very distant\nstar will be finite; if Riemann's is true, it will be negative. These\nare results which seem within the reach of experiment, and there have\nbeen hopes that astronomical observations might enable us to decide\nbetween the three geometries.\n\nBut in astronomy 'straight line' means simply 'path of a ray of light.'\n\nIf therefore negative parallaxes were found, or if it were demonstrated\nthat all parallaxes are superior to a certain limit, two courses would\nbe open to us; we might either renounce Euclidean geometry, or else\nmodify the laws of optics and suppose that light does not travel\nrigorously in a straight line.\n\nIt is needless to add that all the world would regard the latter\nsolution as the more advantageous.\n\nThe Euclidean geometry has, therefore, nothing to fear from fresh\nexperiments.\n\n4. Is the position tenable, that certain phenomena, possible in\nEuclidean space, would be impossible in non-Euclidean space, so that\nexperience, in establishing these phenomena, would directly contradict\nthe non-Euclidean hypothesis? For my part I think no such question can\nbe put. To my mind it is precisely equivalent to the following, whose\nabsurdity is patent to all eyes: are there lengths expressible in meters\nand centimeters, but which can not be measured in fathoms, feet and\ninches, so that experience, in ascertaining the existence of these\nlengths, would directly contradict the hypothesis that there are fathoms\ndivided into six feet?\n\nExamine the question more closely. I suppose that the straight line\npossesses in Euclidean space any two properties which I shall call _A_\nand _B_; that in non-Euclidean space it still possesses the property\n_A_, but no longer has the property _B_; finally I suppose that in both\nEuclidean and non-Euclidean space the straight line is the only line\nhaving the property _A_.\n\nIf this were so, experience would be capable of deciding between the\nhypothesis of Euclid and that of Lobachevski. It would be ascertained\nthat a definite concrete object, accessible to experiment, for example,\na pencil of rays of light, possesses the property _A_; we should\nconclude that it is rectilinear, and then investigate whether or not it\nhas the property _B_.\n\nBut _this is not so_; no property exists which, like this property _A_,\ncan be an absolute criterion enabling us to recognize the straight line\nand to distinguish it from every other line.\n\nShall we say, for instance: \"the following is such a property: the\nstraight line is a line such that a figure of which this line forms a\npart can be moved without the mutual distances of its points varying and\nso that all points of this line remain fixed\"?\n\nThis, in fact, is a property which, in Euclidean or non-Euclidean space,\nbelongs to the straight and belongs only to it. But how shall we\nascertain experimentally whether it belongs to this or that concrete\nobject? It will be necessary to measure distances, and how shall one\nknow that any concrete magnitude which I have measured with my material\ninstrument really represents the abstract distance?\n\nWe have only pushed back the difficulty.\n\nIn reality the property just enunciated is not a property of the\nstraight line alone, it is a property of the straight line and\ndistance. For it to serve as absolute criterion, we should have to be\nable to establish not only that it does not also belong to a line other\nthan the straight and to distance, but in addition that it does not\nbelong to a line other than the straight and to a magnitude other than\ndistance. Now this is not true.\n\nIt is therefore impossible to imagine a concrete experiment which can be\ninterpreted in the Euclidean system and not in the Lobachevskian system,\nso that I may conclude:\n\nNo experience will ever be in contradiction to Euclid's postulate; nor,\non the other hand, will any experience ever contradict the postulate of\nLobachevski.\n\n5. But it is not enough that the Euclidean (or non-Euclidean) geometry\ncan never be directly contradicted by experience. Might it not happen\nthat it can accord with experience only by violating the principle of\nsufficient reason or that of the relativity of space?\n\nI will explain myself: consider any material system; we shall have to\nregard, on the one hand, 'the state' of the various bodies of this\nsystem (for instance, their temperature, their electric potential,\netc.), and, on the other hand, their position in space; and among the\ndata which enable us to define this position we shall, moreover,\ndistinguish the mutual distances of these bodies, which define their\nrelative positions, from the conditions which define the absolute\nposition of the system and its absolute orientation in space.\n\nThe laws of the phenomena which will happen in this system will depend\non the state of these bodies and their mutual distances; but, because of\nthe relativity and passivity of space, they will not depend on the\nabsolute position and orientation of the system.\n\nIn other words, the state of the bodies and their mutual distances at\nany instant will depend solely on the state of these same bodies and on\ntheir mutual distances at the initial instant, but will not at all\ndepend on the absolute initial position of the system or on its absolute\ninitial orientation. This is what for brevity I shall call the _law of\nrelativity_.\n\nHitherto I have spoken as a Euclidean geometer. As I have said, an\nexperience, whatever it be, admits of an interpretation on the Euclidean\nhypothesis; but it admits of one equally on the non-Euclidean\nhypothesis. Well, we have made a series of experiments; we have\ninterpreted them on the Euclidean hypothesis, and we have recognized\nthat these experiments thus interpreted do not violate this 'law of\nrelativity.'\n\nWe now interpret them on the non-Euclidean hypothesis: this is always\npossible; only the non-Euclidean distances of our different bodies in\nthis new interpretation will not generally be the same as the Euclidean\ndistances in the primitive interpretation.\n\nWill our experiments, interpreted in this new manner, still be in accord\nwith our 'law of relativity'? And if there were not this accord, should\nwe not have also the right to say experience had proven the falsity of\nthe non-Euclidean geometry?\n\nIt is easy to see that this is an idle fear; in fact, to apply the law\nof relativity in all rigor, it must be applied to the entire universe.\nFor if only a part of this universe were considered, and if the absolute\nposition of this part happened to vary, the distances to the other\nbodies of the universe would likewise vary, their influence on the part\nof the universe considered would consequently augment or diminish, which\nmight modify the laws of the phenomena happening there.\n\nBut if our system is the entire universe, experience is powerless to\ngive information about its absolute position and orientation in space.\nAll that our instruments, however perfected they may be, can tell us\nwill be the state of the various parts of the universe and their mutual\ndistances.\n\nSo our law of relativity may be thus enunciated:\n\nThe readings we shall be able to make on our instruments at any instant\nwill depend only on the readings we could have made on these same\ninstruments at the initial instant.\n\nNow such an enunciation is independent of every interpretation of\nexperimental facts. If the law is true in the Euclidean interpretation,\nit will also be true in the non-Euclidean interpretation.\n\nAllow me here a short digression. I have spoken above of the data which\ndefine the position of the various bodies of the system; I should\nlikewise have spoken of those which define their velocities; I should\nthen have had to distinguish the velocities with which the mutual\ndistances of the different bodies vary; and, on the other hand, the\nvelocities of translation and rotation of the system, that is to say,\nthe velocities with which its absolute position and orientation vary.\n\nTo fully satisfy the mind, the law of relativity should be expressible\nthus:\n\nThe state of bodies and their mutual distances at any instant, as well\nas the velocities with which these distances vary at this same instant,\nwill depend only on the state of those bodies and their mutual distances\nat the initial instant, and the velocities with which these distances\nvary at this initial instant, but they will not depend either upon the\nabsolute initial position of the system, or upon its absolute\norientation, or upon the velocities with which this absolute position\nand orientation varied at the initial instant.\n\nUnhappily the law thus enunciated is not in accord with experiments, at\nleast as they are ordinarily interpreted.\n\nSuppose a man be transported to a planet whose heavens were always\ncovered with a thick curtain of clouds, so that he could never see the\nother stars; on that planet he would live as if it were isolated in\nspace. Yet this man could become aware that it turned, either by\nmeasuring its oblateness (done ordinarily by the aid of astronomic\nobservations, but capable of being done by purely geodetic means), or by\nrepeating the experiment of Foucault's pendulum. The absolute rotation\nof this planet could therefore be made evident.\n\nThat is a fact which shocks the philosopher, but which the physicist is\ncompelled to accept.\n\nWe know that from this fact Newton inferred the existence of absolute\nspace; I myself am quite unable to adopt this view. I shall explain why\nin Part III. For the moment it is not my intention to enter upon this\ndifficulty.\n\nTherefore I must resign myself, in the enunciation of the law of\nrelativity, to including velocities of every kind among the data which\ndefine the state of the bodies.\n\nHowever that may be, this difficulty is the same for Euclid's geometry\nas for Lobachevski's; I therefore need not trouble myself with it, and\nhave only mentioned it incidentally.\n\nWhat is important is the conclusion: experiment can not decide between\nEuclid and Lobachevski.\n\nTo sum up, whichever way we look at it, it is impossible to discover in\ngeometric empiricism a rational meaning.\n\n6. Experiments only teach us the relations of bodies to one another;\nnone of them bears or can bear on the relations of bodies with space, or\non the mutual relations of different parts of space.\n\n\"Yes,\" you reply, \"a single experiment is insufficient, because it gives\nme only a single equation with several unknowns; but when I shall have\nmade enough experiments I shall have equations enough to calculate all\nmy unknowns.\"\n\nTo know the height of the mainmast does not suffice for calculating the\nage of the captain. When you have measured every bit of wood in the ship\nyou will have many equations, but you will know his age no better. All\nyour measurements bearing only on your bits of wood can reveal to you\nnothing except concerning these bits of wood. Just so your experiments,\nhowever numerous they may be, bearing only on the relations of bodies to\none another, will reveal to us nothing about the mutual relations of the\nvarious parts of space.\n\n7. Will you say that if the experiments bear on the bodies, they bear at\nleast upon the geometric properties of the bodies? But, first, what do\nyou understand by geometric properties of the bodies? I assume that it\nis a question of the relations of the bodies with space; these\nproperties are therefore inaccessible to experiments which bear only on\nthe relations of the bodies to one another. This alone would suffice to\nshow that there can be no question of these properties.\n\nStill let us begin by coming to an understanding about the sense of the\nphrase: geometric properties of bodies. When I say a body is composed of\nseveral parts, I assume that I do not enunciate therein a geometric\nproperty, and this would remain true even if I agreed to give the\nimproper name of points to the smallest parts I consider.\n\nWhen I say that such a part of such a body is in contact with such a\npart of such another body, I enunciate a proposition which concerns the\nmutual relations of these two bodies and not their relations with\nspace.\n\nI suppose you will grant me these are not geometric properties; at least\nI am sure you will grant me these properties are independent of all\nknowledge of metric geometry.\n\nThis presupposed, I imagine that we have a solid body formed of eight\nslender iron rods, _OA_, _OB_, _OC_, _OD_, _OE_, _OF_, _OG_, _OH_,\nunited at one of their extremities _O_. Let us besides have a second\nsolid body, for example a bit of wood, to be marked with three little\nflecks of ink which I shall call [alpha], [beta], [gamma]. I further\nsuppose it ascertained that [alpha][beta][gamma] may be brought into\ncontact with _AGO_ (I mean [alpha] with _A_, and at the same time [beta]\nwith _G_ and [gamma] with _O_), then that we may bring successively into\ncontact [alpha][beta][gamma] with _BGO_, _CGO_, _DGO_, _EGO_, _FGO_,\nthen with _AHO_, _BHO_, _CHO_, _DHO_, _EHO_, _FHO_, then [alpha][gamma]\nsuccessively with _AB_, _BC_, _CD_, _DE_, _EF_, _FA_.\n\nThese are determinations we may make without having in advance any\nnotion about form or about the metric properties of space. They in no\nwise bear on the 'geometric properties of bodies.' And these\ndeterminations will not be possible if the bodies experimented upon move\nin accordance with a group having the same structure as the\nLobachevskian group (I mean according to the same laws as solid bodies\nin Lobachevski's geometry). They suffice therefore to prove that these\nbodies move in accordance with the Euclidean group, or at least that\nthey do not move according to the Lobachevskian group.\n\nThat they are compatible with the Euclidean group is easy to see. For\nthey could be made if the body [alpha][beta][gamma] was a rigid solid of\nour ordinary geometry presenting the form of a right-angled triangle,\nand if the points _ABCDEFGH_ were the summits of a polyhedron formed of\ntwo regular hexagonal pyramids of our ordinary geometry, having for\ncommon base _ABCDEF_ and for apices the one _G_ and the other _H_.\n\nSuppose now that in place of the preceding determination it is observed\nthat as above [alpha][beta][gamma] can be successively applied to _AGO_,\n_BGO_, _CGO_, _DGO_, _EGO_, _AHO_, _BHO_, _CHO_, _DHO_, _EHO_, _FHO_,\nthen that [alpha][beta] (and no longer [alpha][gamma]) can be\nsuccessively applied to _AB_, _BC_, _CD_, _DE_, _EF_ and _FA_.\n\nThese are determinations which could be made if non-Euclidean geometry\nwere true, if the bodies [alpha][beta][gamma] and _OABCDEFGH_ were rigid\nsolids, and if the first were a right-angled triangle and the second a\ndouble regular hexagonal pyramid of suitable dimensions.\n\nTherefore these new determinations are not possible if the bodies move\naccording to the Euclidean group; but they become so if it be supposed\nthat the bodies move according to the Lobachevskian group. They would\nsuffice, therefore (if one made them), to prove that the bodies in\nquestion do not move according to the Euclidean group.\n\nThus, without making any hypothesis about form, about the nature of\nspace, about the relations of bodies to space, and without attributing\nto bodies any geometric property, I have made observations which have\nenabled me to show in one case that the bodies experimented upon move\naccording to a group whose structure is Euclidean, in the other case\nthat they move according to a group whose structure is Lobachevskian.\n\nAnd one may not say that the first aggregate of determinations would\nconstitute an experiment proving that space is Euclidean, and the second\nan experiment proving that space is non-Euclidean.\n\nIn fact one could imagine (I say imagine) bodies moving so as to render\npossible the second series of determinations. And the proof is that the\nfirst mechanician met could construct such bodies if he cared to take\nthe pains and make the outlay. You will not conclude from that, however,\nthat space is non-Euclidean.\n\nNay, since the ordinary solid bodies would continue to exist when the\nmechanician had constructed the strange bodies of which I have just\nspoken, it would be necessary to conclude that space is at the same time\nEuclidean and non-Euclidean.\n\nSuppose, for example, that we have a great sphere of radius _R_ and that\nthe temperature decreases from the center to the surface of this sphere\naccording to the law of which I have spoken in describing the\nnon-Euclidean world.\n\nWe might have bodies whose expansion would be negligible and which would\nact like ordinary rigid solids; and, on the other hand, bodies very\ndilatable and which would act like non-Euclidean solids. We might have\ntwo double pyramids _OABCDEFGH_ and _O'A'B'C'D'E'F'G'H'_ and two\ntriangles [alpha][beta][gamma] and [alpha]'[beta]'[gamma]'. The first\ndouble pyramid might be rectilinear and the second curvilinear; the\ntriangle [alpha][beta][gamma] might be made of inexpansible matter and\nthe other of a very dilatable matter.\n\nIt would then be possible to make the first observations with the double\npyramid _OAH_ and the triangle [alpha][beta][gamma], and the second with\nthe double pyramid _O'A'H'_ and the triangle [alpha]'[beta]'[gamma]'.\nAnd then experiment would seem to prove first that the Euclidean\ngeometry is true and then that it is false.\n\n_Experiments therefore have a bearing, not on space, but on bodies._\n\n\nSUPPLEMENT\n\n8. To complete the matter, I ought to speak of a very delicate question,\nwhich would require long development; I shall confine myself to\nsummarizing here what I have expounded in the _Revue de M\u00e9taphysique et\nde Morale_ and in _The Monist_. When we say space has three dimensions,\nwhat do we mean?\n\nWe have seen the importance of those 'internal changes' revealed to us\nby our muscular sensations. They may serve to characterize the various\n_attitudes_ of our body. Take arbitrarily as origin one of these\nattitudes _A_. When we pass from this initial attitude to any other\nattitude _B_, we feel a series of muscular sensations, and this series\n_S_ will define _B_. Observe, however, that we shall often regard two\nseries _S_ and _S'_ as defining the same attitude _B_ (since the initial\nand final attitudes _A_ and _B_ remaining the same, the intermediary\nattitudes and the corresponding sensations may differ). How then shall\nwe recognize the equivalence of these two series? Because they may serve\nto compensate the same external change, or more generally because, when\nit is a question of compensating an external change, one of the series\ncan be replaced by the other. Among these series, we have distinguished\nthose which of themselves alone can compensate an external change, and\nwhich we have called 'displacements.' As we can not discriminate between\ntwo displacements which are too close together, the totality of these\ndisplacements presents the characteristics of a physical continuum;\nexperience teaches us that they are those of a physical continuum of six\ndimensions; but we do not yet know how many dimensions space itself has,\nwe must first solve another question.\n\nWhat is a point of space? Everybody thinks he knows, but that is an\nillusion. What we see when we try to represent to ourselves a point of\nspace is a black speck on white paper, a speck of chalk on a blackboard,\nalways an object. The question should therefore be understood as\nfollows:\n\nWhat do I mean when I say the object _B_ is at the same point that the\nobject _A_ occupied just now? Or further, what criterion will enable me\nto apprehend this?\n\nI mean that, _although I have not budged_ (which my muscular sense tells\nme), my first finger which just now touched the object _A_ touches at\npresent the object _B_. I could have used other criteria; for instance\nanother finger or the sense of sight. But the first criterion is\nsufficient; I know that if it answers yes, all the other criteria will\ngive the same response. I know it _by experience_, I can not know it _a\npriori_. For the same reason I say that touch can not be exercised at a\ndistance; this is another way of enunciating the same experimental fact.\nAnd if, on the contrary, I say that sight acts at a distance, it means\nthat the criterion furnished by sight may respond yes while the others\nreply no.\n\nAnd in fact, the object, although moved away, may form its image at the\nsame point of the retina. Sight responds yes, the object has remained at\nthe same point and touch answers no, because my finger which just now\ntouched the object, at present touches it no longer. If experience had\nshown us that one finger may respond no when the other says yes, we\nshould likewise say that touch acts at a distance.\n\nIn short, for each attitude of my body, my first finger determines a\npoint, and this it is, and this alone, which defines a point of space.\n\nTo each attitude corresponds thus a point; but it often happens that the\nsame point corresponds to several different attitudes (in this case we\nsay our finger has not budged, but the rest of the body has moved). We\ndistinguish, therefore, among the changes of attitude those where the\nfinger does not budge. How are we led thereto? It is because often we\nnotice that in these changes the object which is in contact with the\nfinger remains in contact with it.\n\nRange, therefore, in the same class all the attitudes obtainable from\neach other by one of the changes we have thus distinguished. To all the\nattitudes of the class will correspond the same point of space.\nTherefore to each class will correspond a point and to each point a\nclass. But one may say that what experience arrives at is not the point,\nit is this class of changes or, better, the corresponding class of\nmuscular sensations.\n\nAnd when we say space has three dimensions, we simply mean that the\ntotality of these classes appears to us with the characteristics of a\nphysical continuum of three dimensions.\n\nOne might be tempted to conclude that it is experience which has taught\nus how many dimensions space has. But in reality here also our\nexperiences have bearing, not on space, but on our body and its\nrelations with the neighboring objects. Moreover they are excessively\ncrude.\n\nIn our mind pre-existed the latent idea of a certain number of\ngroups--those whose theory Lie has developed. Which group shall we\nchoose, to make of it a sort of standard with which to compare natural\nphenomena? And, this group chosen, which of its sub-groups shall we take\nto characterize a point of space? Experience has guided us by showing us\nwhich choice best adapts itself to the properties of our body. But its\nr\u00f4le is limited to that.\n\n\nANCESTRAL EXPERIENCE\n\nIt has often been said that if individual experience could not create\ngeometry the same is not true of ancestral experience. But what does\nthat mean? Is it meant that we could not experimentally demonstrate\nEuclid's postulate, but that our ancestors have been able to do it? Not\nin the least. It is meant that by natural selection our mind has\n_adapted_ itself to the conditions of the external world, that it has\nadopted the geometry _most advantageous_ to the species: or in other\nwords _the most convenient_. This is entirely in conformity with our\nconclusions; geometry is not true, it is advantageous.\n\n\n\n\nPART III\n\n\nFORCE\n\n\n\n\nCHAPTER VI\n\nTHE CLASSIC MECHANICS\n\n\nThe English teach mechanics as an experimental science; on the continent\nit is always expounded as more or less a deductive and _a priori_\nscience. The English are right, that goes without saying; but how could\nthe other method have been persisted in so long? Why have the\ncontinental savants who have sought to get out of the ruts of their\npredecessors been usually unable to free themselves completely?\n\nOn the other hand, if the principles of mechanics are only of\nexperimental origin, are they not therefore only approximate and\nprovisional? Might not new experiments some day lead us to modify or\neven to abandon them?\n\nSuch are the questions which naturally obtrude themselves, and the\ndifficulty of solution comes principally from the fact that the\ntreatises on mechanics do not clearly distinguish between what is\nexperiment, what is mathematical reasoning, what is convention, what is\nhypothesis.\n\nThat is not all:\n\n1\u00ba There is no absolute space and we can conceive only of relative\nmotions; yet usually the mechanical facts are enunciated as if there\nwere an absolute space to which to refer them.\n\n2\u00ba There is no absolute time; to say two durations are equal is an\nassertion which has by itself no meaning and which can acquire one only\nby convention.\n\n3\u00ba Not only have we no direct intuition of the equality of two\ndurations, but we have not even direct intuition of the simultaneity of\ntwo events occurring in different places: this I have explained in an\narticle entitled _La mesure du temps_.[3]\n\n [3] _Revue de M\u00e9taphysique et de Morale_, t. VI., pp. 1-13\n (January, 1898).\n\n4\u00ba Finally, our Euclidean geometry is itself only a sort of convention\nof language; mechanical facts might be enunciated with reference to a\nnon-Euclidean space which would be a guide less convenient than, but\njust as legitimate as, our ordinary space; the enunciation would thus\nbecome much more complicated, but it would remain possible.\n\nThus absolute space, absolute time, geometry itself, are not conditions\nwhich impose themselves on mechanics; all these things are no more\nantecedent to mechanics than the French language is logically antecedent\nto the verities one expresses in French.\n\nWe might try to enunciate the fundamental laws of mechanics in a\nlanguage independent of all these conventions; we should thus without\ndoubt get a better idea of what these laws are in themselves; this is\nwhat M. Andrade has attempted to do, at least in part, in his _Le\u00e7ons de\nm\u00e9canique physique_.\n\nThe enunciation of these laws would become of course much more\ncomplicated, because all these conventions have been devised expressly\nto abridge and simplify this enunciation.\n\nAs for me, save in what concerns absolute space, I shall ignore all\nthese difficulties; not that I fail to appreciate them, far from that;\nbut we have sufficiently examined them in the first two parts of the\nbook.\n\nI shall therefore admit, _provisionally_, absolute time and Euclidean\ngeometry.\n\nTHE PRINCIPLE OF INERTIA.--A body acted on by no force can only move\nuniformly in a straight line.\n\nIs this a truth imposed _a priori_ upon the mind? If it were so, how\nshould the Greeks have failed to recognize it? How could they have\nbelieved that motion stops when the cause which gave birth to it ceases?\nOr again that every body if nothing prevents, will move in a circle, the\nnoblest of motions?\n\nIf it is said that the velocity of a body can not change if there is no\nreason for it to change, could it not be maintained just as well that\nthe position of this body can not change, or that the curvature of its\ntrajectory can not change, if no external cause intervenes to modify\nthem?\n\nIs the principle of inertia, which is not an _a priori_ truth, therefore\nan experimental fact? But has any one ever experimented on bodies\nwithdrawn from the action of every force? and, if so, how was it known\nthat these bodies were subjected to no force? The example ordinarily\ncited is that of a ball rolling a very long time on a marble table; but\nwhy do we say it is subjected to no force? Is this because it is too\nremote from all other bodies to experience any appreciable action from\nthem? Yet it is not farther from the earth than if it were thrown freely\ninto the air; and every one knows that in this case it would experience\nthe influence of gravity due to the attraction of the earth.\n\nTeachers of mechanics usually pass rapidly over the example of the ball;\nbut they add that the principle of inertia is verified indirectly by its\nconsequences. They express themselves badly; they evidently mean it is\npossible to verify various consequences of a more general principle, of\nwhich that of inertia is only a particular case.\n\nI shall propose for this general principle the following enunciation:\n\nThe acceleration of a body depends only upon the position of this body\nand of the neighboring bodies and upon their velocities.\n\nMathematicians would say the movements of all the material molecules of\nthe universe depend on differential equations of the second order.\n\nTo make it clear that this is really the natural generalization of the\nlaw of inertia, I shall beg you to permit me a bit of fiction. The law\nof inertia, as I have said above, is not imposed upon us _a priori_;\nother laws would be quite as compatible with the principle of sufficient\nreason. If a body is subjected to no force, in lieu of supposing its\nvelocity not to change, it might be supposed that it is its position or\nelse its acceleration which is not to change.\n\nWell, imagine for an instant that one of these two hypothetical laws is\na law of nature and replaces our law of inertia. What would be its\nnatural generalization? A moment's thought will show us.\n\nIn the first case, we must suppose that the velocity of a body depends\nonly upon its position and upon that of the neighboring bodies; in the\nsecond case that the change of acceleration of a body depends only upon\nthe position of this body and of the neighboring bodies, upon their\nvelocities and upon their accelerations.\n\nOr to speak the language of mathematics, the differential equations of\nmotion would be of the first order in the first case, and of the third\norder in the second case.\n\nLet us slightly modify our fiction. Suppose a world analogous to our\nsolar system, but where, by a strange chance, the orbits of all the\nplanets are without eccentricity and without inclination. Suppose\nfurther that the masses of these planets are too slight for their mutual\nperturbations to be sensible. Astronomers inhabiting one of these\nplanets could not fail to conclude that the orbit of a star can only be\ncircular and parallel to a certain plane; the position of a star at a\ngiven instant would then suffice to determine its velocity and its whole\npath. The law of inertia which they would adopt would be the first of\nthe two hypothetical laws I have mentioned.\n\nImagine now that this system is some day traversed with great velocity\nby a body of vast mass, coming from distant constellations. All the\norbits would be profoundly disturbed. Still our astronomers would not be\ntoo greatly astonished; they would very well divine that this new star\nwas alone to blame for all the mischief. \"But,\" they would say, \"when it\nis gone, order will of itself be reestablished; no doubt the distances\nof the planets from the sun will not revert to what they were before the\ncataclysm, but when the perturbing star is gone, the orbits will again\nbecome circular.\"\n\nIt would only be when the disturbing body was gone and when nevertheless\nthe orbits, in lieu of again becoming circular, became elliptic, that\nthese astronomers would become conscious of their error and the\nnecessity of remaking all their mechanics.\n\nI have dwelt somewhat upon these hypotheses because it seems to me one\ncan clearly comprehend what our generalized law of inertia really is\nonly in contrasting it with a contrary hypothesis.\n\nWell, now, has this generalized law of inertia been verified by\nexperiment, or can it be? When Newton wrote the _Principia_ he quite\nregarded this truth as experimentally acquired and demonstrated. It was\nso in his eyes, not only through the anthropomorphism of which we shall\nspeak further on, but through the work of Galileo. It was so even from\nKepler's laws themselves; in accordance with these laws, in fact, the\npath of a planet is completely determined by its initial position and\ninitial velocity; this is just what our generalized law of inertia\nrequires.\n\nFor this principle to be only in appearance true, for one to have cause\nto dread having some day to replace it by one of the analogous\nprinciples I have just now contrasted with it, would be necessary our\nhaving been misled by some amazing chance, like that which, in the\nfiction above developed, led into error our imaginary astronomers.\n\nSuch a hypothesis is too unlikely to delay over. No one will believe\nthat such coincidences can happen; no doubt the probability of two\neccentricities being both precisely null, to within errors of\nobservation, is not less than the probability of one being precisely\nequal to 0.1, for instance, and the other to 0.2, to within errors of\nobservation. The probability of a simple event is not less than that of\na complicated event; and yet, if the first happens, we shall not consent\nto attribute it to chance; we should not believe that nature had acted\nexpressly to deceive us. The hypothesis of an error of this sort being\ndiscarded, it may therefore be admitted that in so far as astronomy is\nconcerned, our law has been verified by experiment.\n\nBut astronomy is not the whole of physics.\n\nMay we not fear lest some day a new experiment should come to falsify\nthe law in some domain of physics? An experimental law is always subject\nto revision; one should always expect to see it replaced by a more\nprecise law.\n\nYet no one seriously thinks that the law we are speaking of will ever be\nabandoned or amended. Why? Precisely because it can never be subjected\nto a decisive test.\n\nFirst of all, in order that this trial should be complete, it would be\nnecessary that after a certain time all the bodies in the universe\nshould revert to their initial positions with their initial velocities.\nIt might then be seen whether, starting from this moment, they would\nresume their original paths.\n\nBut this test is impossible, it can be only partially applied, and,\nhowever well it is made, there will always be some bodies which will not\nrevert to their initial positions; thus every derogation of the law will\neasily find its explanation.\n\nThis is not all; in astronomy we _see_ the bodies whose motions we study\nand we usually assume that they are not subjected to the action of other\ninvisible bodies. Under these conditions our law must indeed be either\nverified or not verified.\n\nBut it is not the same in physics; if the physical phenomena are due to\nmotions, it is to the motions of molecules which we do not see. If then\nthe acceleration of one of the bodies we see appears to us to depend on\n_something else_ besides the positions or velocities of other visible\nbodies or of invisible molecules whose existence we have been previously\nled to admit, nothing prevents our supposing that this _something else_\nis the position or the velocity of other molecules whose presence we\nhave not before suspected. The law will find itself safeguarded.\n\nPermit me to employ mathematical language a moment to express the same\nthought under another form. Suppose we observe _n_ molecules and\nascertain that their 3_n_ coordinates satisfy a system of 3_n_\ndifferential equations of the fourth order (and not of the second order\nas the law of inertia would require). We know that by introducing 3_n_\nauxiliary variables, a system of 3_n_ equations of the fourth order can\nbe reduced to a system of 6_n_ equations of the second order. If then we\nsuppose these 3_n_ auxiliary variables represent the coordinates of _n_\ninvisible molecules, the result is again in conformity with the law of\ninertia.\n\nTo sum up, this law, verified experimentally in some particular cases,\nmay unhesitatingly be extended to the most general cases, since we know\nthat in these general cases experiment no longer is able either to\nconfirm or to contradict it.\n\nTHE LAW OF ACCELERATION.--The acceleration of a body is equal to the\nforce acting on it divided by its mass. Can this law be verified by\nexperiment? For that it would be necessary to measure the three\nmagnitudes which figure in the enunciation: acceleration, force and\nmass.\n\nI assume that acceleration can be measured, for I pass over the\ndifficulty arising from the measurement of time. But how measure force,\nor mass? We do not even know what they are.\n\nWhat is _mass_? According to Newton, it is the product of the volume by\nthe density. According to Thomson and Tait, it would be better to say\nthat density is the quotient of the mass by the volume. What is _force_?\nIt is, replies Lagrange, that which moves or tends to move a body. It\nis, Kirchhoff will say, the product of the mass by the _acceleration_.\nBut then, why not say the mass is the quotient of the force by the\nacceleration?\n\nThese difficulties are inextricable.\n\nWhen we say force is the cause of motion, we talk metaphysics, and this\ndefinition, if one were content with it, would be absolutely sterile.\nFor a definition to be of any use, it must teach us to _measure_ force;\nmoreover that suffices; it is not at all necessary that it teach us what\nforce is _in itself_, nor whether it is the cause or the effect of\nmotion.\n\nWe must therefore first define the equality of two forces. When shall we\nsay two forces are equal? It is, we are told, when, applied to the same\nmass, they impress upon it the same acceleration, or when, opposed\ndirectly one to the other, they produce equilibrium. This definition is\nonly a sham. A force applied to a body can not be uncoupled to hook it\nup to another body, as one uncouples a locomotive to attach it to\nanother train. It is therefore impossible to know what acceleration such\na force, applied to such a body, would impress upon such another body,\n_if_ it were applied to it. It is impossible to know how two forces\nwhich are not directly opposed would act, _if_ they were directly\nopposed.\n\nIt is this definition we try to materialize, so to speak, when we\nmeasure a force with a dynamometer, or in balancing it with a weight.\nTwo forces _F_ and _F'_, which for simplicity I will suppose vertical\nand directed upward, are applied respectively to two bodies _C_ and\n_C'_; I suspend the same heavy body _P_ first to the body _C_, then to\nthe body _C'_; if equilibrium is produced in both cases, I shall\nconclude that the two forces _F_ and _F'_ are equal to one another,\nsince they are each equal to the weight of the body _P_.\n\nBut am I sure the body _P_ has retained the same weight when I have\ntransported it from the first body to the second? Far from it; _I am\nsure of the contrary_; I know the intensity of gravity varies from one\npoint to another, and that it is stronger, for instance, at the pole\nthan at the equator. No doubt the difference is very slight and, in\npractise, I shall take no account of it; but a properly constructed\ndefinition should have mathematical rigor; this rigor is lacking. What I\nsay of weight would evidently apply to the force of the resiliency of a\ndynamometer, which the temperature and a multitude of circumstances may\ncause to vary.\n\nThis is not all; we can not say the weight of the body _P_ may be\napplied to the body _C_ and directly balance the force _F_. What is\napplied to the body _C_ is the action _A_ of the body _P_ on the body\n_C_; the body _P_ is submitted on its part, on the one hand, to its\nweight; on the other hand, to the reaction _R_ of the body _C_ on _P_.\nFinally, the force _F_ is equal to the force _A_, since it balances it;\nthe force _A_ is equal to _R_, in virtue of the principle of the\nequality of action and reaction; lastly, the force _R_ is equal to the\nweight of _P_, since it balances it. It is from these three equalities\nwe deduce as consequence the equality of _F_ and the weight of _P_.\n\nWe are therefore obliged in the definition of the equality of the two\nforces to bring in the principle of the equality of action and reaction;\n_on this account, this principle must no longer be regarded as an\nexperimental law, but as a definition_.\n\nFor recognizing the equality of two forces here, we are then in\npossession of two rules: equality of two forces which balance; equality\nof action and reaction. But, as we have seen above, these two rules are\ninsufficient; we are obliged to have recourse to a third rule and to\nassume that certain forces, as, for instance, the weight of a body, are\nconstant in magnitude and direction. But this third rule, as I have\nsaid, is an experimental law; it is only approximately true; _it is a\nbad definition_.\n\nWe are therefore reduced to Kirchhoff's definition; _force is equal to\nthe mass multiplied by the acceleration_. This 'law of Newton' in its\nturn ceases to be regarded as an experimental law, it is now only a\ndefinition. But this definition is still insufficient, for we do not\nknow what mass is. It enables us doubtless to calculate the relation of\ntwo forces applied to the same body at different instants; it teaches us\nnothing about the relation of two forces applied to two different\nbodies.\n\nTo complete it, it is necessary to go back anew to Newton's third law\n(equality of action and reaction), regarded again, not as an\nexperimental law, but as a definition. Two bodies _A_ and _B_ act one\nupon the other; the acceleration of _A_ multiplied by the mass of _A_ is\nequal to the action of _B_ upon _A_; in the same way, the product of the\nacceleration of _B_ by its mass is equal to the reaction of _A_ upon\n_B_. As, by definition, action is equal to reaction, the masses of _A_\nand _B_ are in the inverse ratio of their accelerations. Here we have\nthe ratio of these two masses defined, and it is for experiment to\nverify that this ratio is constant.\n\nThat would be all very well if the two bodies _A_ and _B_ alone were\npresent and removed from the action of the rest of the world. This is\nnot at all the case; the acceleration of _A_ is not due merely to the\naction of _B_, but to that of a multitude of other bodies _C_, _D_,...\nTo apply the preceding rule, it is therefore necessary to separate the\nacceleration of _A_ into many components, and discern which of these\ncomponents is due to the action of _B_.\n\nThis separation would still be possible, if we _should assume_ that the\naction of _C_ upon _A_ is simply adjoined to that of _B_ upon _A_,\nwithout the presence of the body _C_ modifying the action of _B_ upon\n_A_; or the presence of _B_ modifying the action of _C_ upon _A_; if we\nshould assume, consequently, that any two bodies attract each other,\nthat their mutual action is along their join and depends only upon their\ndistance apart; if, in a word, we assume _the hypothesis of central\nforces_.\n\nYou know that to determine the masses of the celestial bodies we use a\nwholly different principle. The law of gravitation teaches us that the\nattraction of two bodies is proportional to their masses; if _r_ is\ntheir distance apart, _m_ and _m'_ their masses, _k_ a constant, their\nattraction will be _kmm'_/_r_^{2}.\n\nWhat we are measuring then is not mass, the ratio of force to\nacceleration, but the attracting mass; it is not the inertia of the\nbody, but its attracting force.\n\nThis is an indirect procedure, whose employment is not theoretically\nindispensable. It might very well have been that attraction was\ninversely proportional to the square of the distance without being\nproportional to the product of the masses, that it was equal\nto _f_/_r_^{2}, but without our having _f_ = _kmm'_.\n\nIf it were so, we could nevertheless, by observation of the _relative_\nmotions of the heavenly bodies, measure the masses of these bodies.\n\nBut have we the right to admit the hypothesis of central forces? Is this\nhypothesis rigorously exact? Is it certain it will never be contradicted\nby experiment? Who would dare affirm that? And if we must abandon this\nhypothesis, the whole edifice so laboriously erected will crumble.\n\nWe have no longer the right to speak of the component of the\nacceleration of _A_ due to the action of _B_. We have no means of\ndistinguishing it from that due to the action of _C_ or of another body.\nThe rule for the measurement of masses becomes inapplicable.\n\nWhat remains then of the principle of the equality of action and\nreaction? If the hypothesis of central forces is rejected, this\nprinciple should evidently be enunciated thus: the geometric resultant\nof all the forces applied to the various bodies of a system isolated\nfrom all external action will be null. Or, in other words, _the motion\nof the center of gravity of this system will be rectilinear and\nuniform_.\n\nThere it seems we have a means of defining mass; the position of the\ncenter of gravity evidently depends on the values attributed to the\nmasses; it will be necessary to dispose of these values in such a way\nthat the motion of the center of gravity may be rectilinear and uniform;\nthis will always be possible if Newton's third law is true, and possible\nin general only in a single way.\n\nBut there exists no system isolated from all external action; all the\nparts of the universe are subject more or less to the action of all the\nother parts. _The law of the motion of the center of gravity is\nrigorously true only if applied to the entire universe._\n\nBut then, to get from it the values of the masses, it would be necessary\nto observe the motion of the center of gravity of the universe. The\nabsurdity of this consequence is manifest; we know only relative\nmotions; the motion of the center of gravity of the universe will remain\nfor us eternally unknown.\n\nTherefore nothing remains and our efforts have been fruitless; we are\ndriven to the following definition, which is only an avowal of\npowerlessness: _masses are coefficients it is convenient to introduce\ninto calculations_.\n\nWe could reconstruct all mechanics by attributing different values to\nall the masses. This new mechanics would not be in contradiction either\nwith experience or with the general principles of dynamics (principle of\ninertia, proportionality of forces to masses and to accelerations,\nequality of action and reaction, rectilinear and uniform motion of the\ncenter of gravity, principle of areas).\n\nOnly the equations of this new mechanics would be _less simple_. Let us\nunderstand clearly: it would only be the first terms which would be less\nsimple, that is those experience has already made us acquainted with;\nperhaps one could alter the masses by small quantities without the\n_complete_ equations gaining or losing in simplicity.\n\nHertz has raised the question whether the principles of mechanics are\nrigorously true. \"In the opinion of many physicists,\" he says, \"it is\ninconceivable that the remotest experience should ever change anything\nin the immovable principles of mechanics; and yet, what comes from\nexperience may always be rectified by experience.\" After what we have\njust said, these fears will appear groundless.\n\nThe principles of dynamics at first appeared to us as experimental\ntruths; but we have been obliged to use them as definitions. It is _by\ndefinition_ that force is equal to the product of mass by acceleration;\nhere, then, is a principle which is henceforth beyond the reach of any\nfurther experiment. It is in the same way by definition that action is\nequal to reaction.\n\nBut then, it will be said, these unverifiable principles are absolutely\ndevoid of any significance; experiment can not contradict them; but they\ncan teach us nothing useful; then what is the use of studying dynamics?\n\nThis over-hasty condemnation would be unjust. There is not in nature any\nsystem _perfectly_ isolated, perfectly removed from all external action;\nbut there are systems _almost_ isolated.\n\nIf such a system be observed, one may study not only the relative\nmotion of its various parts one in reference to another, but also the\nmotion of its center of gravity in reference to the other parts of the\nuniverse. We ascertain then that the motion of this center of gravity is\n_almost_ rectilinear and uniform, in conformity with Newton's third law.\n\nThat is an experimental truth, but it can not be invalidated by\nexperience; in fact, what would a more precise experiment teach us? It\nwould teach us that the law was only almost true; but that we knew\nalready.\n\n_We can now understand how experience has been able to serve as basis\nfor the principles of mechanics and yet will never be able to contradict\nthem._\n\nANTHROPOMORPHIC MECHANICS.--\"Kirchhoff,\" it will be said, \"has only\nacted in obedience to the general tendency of mathematicians toward\nnominalism; from this his ability as a physicist has not saved him. He\nwanted a definition of force, and he took for it the first proposition\nthat presented itself; but we need no definition of force: the idea of\nforce is primitive, irreducible, indefinable; we all know what it is, we\nhave a direct intuition of it. This direct intuition comes from the\nnotion of effort, which is familiar to us from infancy.\"\n\nBut first, even though this direct intuition made known to us the real\nnature of force in itself, it would be insufficient as a foundation for\nmechanics; it would besides be wholly useless. What is of importance is\nnot to know what force is, but to know how to measure it.\n\nWhatever does not teach us to measure it is as useless to mechanics as\nis, for instance, the subjective notion of warmth and cold to the\nphysicist who is studying heat. This subjective notion can not be\ntranslated into numbers, therefore it is of no use; a scientist whose\nskin was an absolutely bad conductor of heat and who, consequently,\nwould never have felt either sensations of cold or sensations of warmth,\ncould read a thermometer just as well as any one else, and that would\nsuffice him for constructing the whole theory of heat.\n\nNow this immediate notion of effort is of no use to us for measuring\nforce; it is clear, for instance, that I should feel more fatigue in\nlifting a weight of fifty kilos than a man accustomed to carry burdens.\n\nBut more than that: this notion of effort does not teach us the real\nnature of force; it reduces itself finally to a remembrance of muscular\nsensations, and it will hardly be maintained that the sun feels a\nmuscular sensation when it draws the earth.\n\nAll that can there be sought is a symbol, less precise and less\nconvenient than the arrows the geometers use, but just as remote from\nthe reality.\n\nAnthropomorphism has played a considerable historic r\u00f4le in the genesis\nof mechanics; perhaps it will still at times furnish a symbol which will\nappear convenient to some minds; but it can not serve as foundation for\nanything of a truly scientific or philosophic character.\n\n'THE SCHOOL OF THE THREAD.'--M. Andrade, in his _Le\u00e7ons de m\u00e9canique\nphysique_, has rejuvenated anthropomorphic mechanics. To the school of\nmechanics to which Kirchhoff belongs, he opposes that which he bizarrely\ncalls the school of the thread.\n\nThis school tries to reduce everything to \"the consideration of certain\nmaterial systems of negligible mass, envisaged in the state of tension\nand capable of transmitting considerable efforts to distant bodies,\nsystems of which the ideal type is the _thread_.\"\n\nA thread which transmits any force is slightly elongated under the\naction of this force; the direction of the thread tells us the direction\nof the force, whose magnitude is measured by the elongation of the\nthread.\n\nOne may then conceive an experiment such as this. A body _A_ is attached\nto a thread; at the other extremity of the thread any force acts which\nvaries until the thread takes an elongation [alpha]; the acceleration of\nthe body _A_ is noted; _A_ is detached and the body _B_ attached to the\nsame thread; the same force or another force acts anew, and is made to\nvary until the thread takes again the elongation [alpha]; the\nacceleration of the body _B_ is noted. The experiment is then renewed\nwith both _A_ and _B_, but so that the thread takes the elongation\n[beta]. The four observed accelerations should be proportional. We have\nthus an experimental verification of the law of acceleration above\nenunciated.\n\nOr still better, a body is submitted to the simultaneous action of\nseveral identical threads in equal tension, and by experiment it is\nsought what must be the orientations of all these threads that the body\nmay remain in equilibrium. We have then an experimental verification of\nthe law of the composition of forces.\n\nBut, after all, what have we done? We have defined the force to which\nthe thread is subjected by the deformation undergone by this thread,\nwhich is reasonable enough; we have further assumed that if a body is\nattached to this thread, the effort transmitted to it by the thread is\nequal to the action this body exercises on this thread; after all, we\nhave therefore used the principle of the equality of action and\nreaction, in considering it, not as an experimental truth, but as the\nvery definition of force.\n\nThis definition is just as conventional as Kirchhoff's, but far less\ngeneral.\n\nAll forces are not transmitted by threads (besides, to be able to\ncompare them, they would all have to be transmitted by identical\nthreads). Even if it should be conceded that the earth is attached to\nthe sun by some invisible thread, at least it would be admitted that we\nhave no means of measuring its elongation.\n\nNine times out of ten, consequently, our definition would be at fault;\nno sort of sense could be attributed to it, and it would be necessary to\nfall back on Kirchhoff's.\n\nWhy then take this d\u00e9tour? You admit a certain definition of force which\nhas a meaning only in certain particular cases. In these cases you\nverify by experiment that it leads to the law of acceleration. On the\nstrength of this experiment, you then take the law of acceleration as a\ndefinition of force in all the other cases.\n\nWould it not be simpler to consider the law of acceleration as a\ndefinition in all cases, and to regard the experiments in question, not\nas verifications of this law, but as verifications of the principle of\nreaction, or as demonstrating that the deformations of an elastic body\ndepend only on the forces to which this body is subjected?\n\nAnd this is without taking into account that the conditions under which\nyour definition could be accepted are never fulfilled except\nimperfectly, that a thread is never without mass, that it is never\nremoved from every force except the reaction of the bodies attached to\nits extremities.\n\nAndrade's ideas are nevertheless very interesting; if they do not\nsatisfy our logical craving, they make us understand better the historic\ngenesis of the fundamental ideas of mechanics. The reflections they\nsuggest show us how the human mind has raised itself from a na\u00efve\nanthropomorphism to the present conceptions of science.\n\nWe see at the start a very particular and in sum rather crude\nexperiment; at the finish, a law perfectly general, perfectly precise,\nthe certainty of which we regard as absolute. This certainty we\nourselves have bestowed upon it voluntarily, so to speak, by looking\nupon it as a convention.\n\nAre the law of acceleration, the rule of the composition of forces then\nonly arbitrary conventions? Conventions, yes; arbitrary, no; they would\nbe if we lost sight of the experiments which led the creators of the\nscience to adopt them, and which, imperfect as they may be, suffice to\njustify them. It is well that from time to time our attention is carried\nback to the experimental origin of these conventions.\n\n\n\n\nCHAPTER VII\n\nRELATIVE MOTION AND ABSOLUTE MOTION\n\n\nTHE PRINCIPLE OF RELATIVE MOTION.--The attempt has sometimes been made\nto attach the law of acceleration to a more general principle. The\nmotion of any system must obey the same laws, whether it be referred to\nfixed axes, or to movable axes carried along in a rectilinear and\nuniform motion. This is the principle of relative motion, which forces\nitself upon us for two reasons: first, the commonest experience confirms\nit, and second, the contrary hypothesis is singularly repugnant to the\nmind.\n\nAssume it then, and consider a body subjected to a force; the relative\nmotion of this body, in reference to an observer moving with a uniform\nvelocity equal to the initial velocity of the body, must be identical to\nwhat its absolute motion would be if it started from rest. We conclude\nhence that its acceleration can not depend upon its absolute velocity;\nthe attempt has even been made to derive from this a demonstration of\nthe law of acceleration.\n\nThere long were traces of this demonstration in the regulations for the\ndegree B. \u00e8s Sc. It is evident that this attempt is idle. The obstacle\nwhich prevented our demonstrating the law of acceleration is that we had\nno definition of force; this obstacle subsists in its entirety, since\nthe principle invoked has not furnished us the definition we lacked.\n\nThe principle of relative motion is none the less highly interesting and\ndeserves study for its own sake. Let us first try to enunciate it in a\nprecise manner.\n\nWe have said above that the accelerations of the different bodies\nforming part of an isolated system depend only on their relative\nvelocities and positions, and not on their absolute velocities and\npositions, provided the movable axes to which the relative motion is\nreferred move uniformly in a straight line. Or, if we prefer, their\naccelerations depend only on the differences of their velocities and the\ndifferences of their coordinates, and not on the absolute values of\nthese velocities and coordinates.\n\nIf this principle is true for relative accelerations, or rather for\ndifferences of acceleration, in combining it with the law of reaction we\nshall thence deduce that it is still true of absolute accelerations.\n\nIt then remains to be seen how we may demonstrate that the differences\nof the accelerations depend only on the differences of the velocities\nand of the coordinates, or, to speak in mathematical language, that\nthese differences of coordinates satisfy differential equations of the\nsecond order.\n\nCan this demonstration be deduced from experiments or from _a priori_\nconsiderations?\n\nRecalling what we have said above, the reader can answer for himself.\n\nThus enunciated, in fact, the principle of relative motion singularly\nresembles what I called above the generalized principle of inertia; it\nis not altogether the same thing, since it is a question of the\ndifferences of coordinates and not of the coordinates themselves. The\nnew principle teaches us therefore something more than the old, but the\nsame discussion is applicable and would lead to the same conclusions; it\nis unnecessary to return to it.\n\nNEWTON'S ARGUMENT.--Here we encounter a very important and even somewhat\ndisconcerting question. I have said the principle of relative motion was\nfor us not solely a result of experiment and that _a priori_ every\ncontrary hypothesis would be repugnant to the mind.\n\nBut then, why is the principle true only if the motion of the movable\naxes is rectilinear and uniform? It seems that it ought to impose itself\nupon us with the same force, if this motion is varied, or at any rate if\nit reduces to a uniform rotation. Now, in these two cases, the principle\nis not true. I will not dwell long on the case where the motion of the\naxes is rectilinear without being uniform; the paradox does not bear a\nmoment's examination. If I am on board, and if the train, striking any\nobstacle, stops suddenly, I shall be thrown against the seat in front of\nme, although I have not been directly subjected to any force. There is\nnothing mysterious in that; if I have undergone the action of no\nexternal force, the train itself has experienced an external impact.\nThere can be nothing paradoxical in the relative motion of two bodies\nbeing disturbed when the motion of one or the other is modified by an\nexternal cause.\n\nI will pause longer on the case of relative motions referred to axes\nwhich rotate uniformly. If the heavens were always covered with clouds,\nif we had no means of observing the stars, we nevertheless might\nconclude that the earth turns round; we could learn this from its\nflattening or again by the Foucault pendulum experiment.\n\nAnd yet, in this case, would it have any meaning, to say the earth turns\nround? If there is no absolute space, can one turn without turning in\nreference to something else? and, on the other hand, how could we admit\nNewton's conclusion and believe in absolute space?\n\nBut it does not suffice to ascertain that all possible solutions are\nequally repugnant to us; we must analyze, in each case, the reasons for\nour repugnance, so as to make our choice intelligently. The long\ndiscussion which follows will therefore be excused.\n\nLet us resume our fiction: thick clouds hide the stars from men, who can\nnot observe them and are ignorant even of their existence; how shall\nthese men know the earth turns round?\n\nEven more than our ancestors, no doubt, they will regard the ground\nwhich bears them as fixed and immovable; they will await much longer the\nadvent of a Copernicus. But in the end the Copernicus would come--how?\n\nThe students of mechanics in this world would not at first be confronted\nwith an absolute contradiction. In the theory of relative motion,\nbesides real forces, two fictitious forces are met which are called\nordinary and compound centrifugal force. Our imaginary scientists could\ntherefore explain everything by regarding these two forces as real, and\nthey would not see therein any contradiction of the generalized\nprinciple of inertia, for these forces would depend, the one on the\nrelative positions of the various parts of the system, as real\nattractions do, the other on their relative velocities, as real\nfrictions do.\n\nMany difficulties, however, would soon awaken their attention; if they\nsucceeded in realizing an isolated system, the center of gravity of this\nsystem would not have an almost rectilinear path. They would invoke, to\nexplain this fact, the centrifugal forces which they would regard as\nreal, and which they would attribute no doubt to the mutual actions of\nthe bodies. Only they would not see these forces become null at great\ndistances, that is to say in proportion as the isolation was better\nrealized; far from it; centrifugal force increases indefinitely with the\ndistance.\n\nThis difficulty would seem to them already sufficiently great; and yet\nit would not stop them long; they would soon imagine some very subtile\nmedium, analogous to our ether, in which all bodies would be immersed\nand which would exert a repellent action upon them.\n\nBut this is not all. Space is symmetric, and yet the laws of motion\nwould not show any symmetry; they would have to distinguish between\nright and left. It would be seen for instance that cyclones turn always\nin the same sense, whereas by reason of symmetry these winds should turn\nindifferently in one sense and in the other. If our scientists by their\nlabor had succeeded in rendering their universe perfectly symmetric,\nthis symmetry would not remain, even though there was no apparent reason\nwhy it should be disturbed in one sense rather than in the other.\n\nThey would get themselves out of the difficulty doubtless, they would\ninvent something which would be no more extraordinary than the glass\nspheres of Ptolemy, and so it would go on, complications accumulating,\nuntil the long-expected Copernicus sweeps them all away at a single\nstroke, saying: It is much simpler to assume the earth turns round.\n\nAnd just as our Copernicus said to us: It is more convenient to suppose\nthe earth turns round, since thus the laws of astronomy are expressible\nin a much simpler language; this one would say: It is more convenient to\nsuppose the earth turns round, since thus the laws of mechanics are\nexpressible in a much simpler language.\n\nThis does not preclude maintaining that absolute space, that is to say\nthe mark to which it would be necessary to refer the earth to know\nwhether it really moves, has no objective existence. Hence, this\naffirmation: 'the earth turns round' has no meaning, since it can be\nverified by no experiment; since such an experiment, not only could not\nbe either realized or dreamed by the boldest Jules Verne, but can not be\nconceived of without contradiction; or rather these two propositions:\n'the earth turns round,' and, 'it is more convenient to suppose the\nearth turns round' have the same meaning; there is nothing more in the\none than in the other.\n\nPerhaps one will not be content even with that, and will find it already\nshocking that among all the hypotheses, or rather all the conventions we\ncan make on this subject, there is one more convenient than the others.\n\nBut if it has been admitted without difficulty when it was a question of\nthe laws of astronomy, why should it be shocking in that which concerns\nmechanics?\n\nWe have seen that the coordinates of bodies are determined by\ndifferential equations of the second order, and that so are the\ndifferences of these coordinates. This is what we have called the\ngeneralized principle of inertia and the principle of relative motion.\nIf the distances of these bodies were determined likewise by equations\nof the second order, it seems that the mind ought to be entirely\nsatisfied. In what measure does the mind get this satisfaction and why\nis it not content with it?\n\nTo account for this, we had better take a simple example. I suppose a\nsystem analogous to our solar system, but where one can not perceive\nfixed stars foreign to this system, so that astronomers can observe only\nthe mutual distances of the planets and the sun, and not the absolute\nlongitudes of the planets. If we deduce directly from Newton's law the\ndifferential equations which define the variation of these distances,\nthese equations will not be of the second order. I mean that if, besides\nNewton's law, one knew the initial values of these distances and of\ntheir derivatives with respect to the time, that would not suffice to\ndetermine the values of these same distances at a subsequent instant.\nThere would still be lacking one datum, and this datum might be for\ninstance what astronomers call the area-constant.\n\nBut here two different points of view may be taken; we may distinguish\ntwo sorts of constants. To the eyes of the physicist the world reduces\nto a series of phenomena, depending, on the one hand, solely upon the\ninitial phenomena; on the other hand, upon the laws which bind the\nconsequents to the antecedents. If then observation teaches us that a\ncertain quantity is a constant, we shall have the choice between two\nconceptions.\n\nEither we shall assume that there is a law requiring this quantity not\nto vary, but that by chance, at the beginning of the ages, it had,\nrather than another, this value it has been forced to keep ever since.\nThis quantity might then be called an _accidental_ constant.\n\nOr else we shall assume, on the contrary, that there is a law of nature\nwhich imposes upon this quantity such a value and not such another.\n\nWe shall then have what we may call an _essential_ constant.\n\nFor example, in virtue of Newton's laws, the duration of the revolution\nof the earth must be constant. But if it is 366 sidereal days and\nsomething over, and not 300 or 400, this is in consequence of I know not\nwhat initial chance. This is an accidental constant. If, on the\ncontrary, the exponent of the distance which figures in the expression\nof the attractive force is equal to -2 and not to -3, this is not by\nchance, but because Newton's law requires it. This is an essential\nconstant.\n\nI know not whether this way of giving chance its part is legitimate in\nitself, and whether this distinction is not somewhat artificial; it is\ncertain at least that, so long as nature shall have secrets, this\ndistinction will be in application extremely arbitrary and always\nprecarious.\n\nAs to the area-constant, we are accustomed to regard it as accidental.\nIs it certain our imaginary astronomers would do the same? If they could\nhave compared two different solar systems, they would have the idea that\nthis constant may have several different values; but my very supposition\nin the beginning was that their system should appear as isolated, and\nthat they should observe no star foreign to it. Under these conditions,\nthey would see only one single constant which would have a single value\nabsolutely invariable; they would be led without any doubt to regard it\nas an essential constant.\n\nA word in passing to forestall an objection: the inhabitants of this\nimaginary world could neither observe nor define the area-constant as we\ndo, since the absolute longitudes escape them; that would not preclude\ntheir being quickly led to notice a certain constant which would\nintroduce itself naturally into their equations and which would be\nnothing but what we call the area-constant.\n\nBut then see what would happen. If the area-constant is regarded as\nessential, as depending upon a law of nature, to calculate the distances\nof the planets at any instant it will suffice to know the initial values\nof these distances and those of their first derivatives. From this new\npoint of view, the distances will be determined by differential\nequations of the second order.\n\nYet would the mind of these astronomers be completely satisfied? I do\nnot believe so; first, they would soon perceive that in differentiating\ntheir equations and thus raising their order, these equations became\nmuch simpler. And above all they would be struck by the difficulty which\ncomes from symmetry. It would be necessary to assume different laws,\naccording as the aggregate of the planets presented the figure of a\ncertain polyhedron or of the symmetric polyhedron, and one would escape\nfrom this consequence only by regarding the area-constant as accidental.\n\nI have taken a very special example, since I have supposed astronomers\nwho did not at all consider terrestrial mechanics, and whose view was\nlimited to the solar system. Our universe is more extended than theirs,\nas we have fixed stars, but still it too is limited, and so we might\nreason on the totality of our universe as the astronomers on their solar\nsystem.\n\nThus we see that finally we should be led to conclude that the equations\nwhich define distances are of an order superior to the second. Why\nshould we be shocked at that, why do we find it perfectly natural for\nthe series of phenomena to depend upon the initial values of the first\nderivatives of these distances, while we hesitate to admit that they may\ndepend on the initial values of the second derivatives? This can only be\nbecause of the habits of mind created in us by the constant study of the\ngeneralized principle of inertia and its consequences.\n\nThe values of the distances at any instant depend upon their initial\nvalues, upon those of their first derivatives and also upon something\nelse. What is this _something else_?\n\nIf we will not admit that this may be simply one of the second\nderivatives, we have only the choice of hypotheses. Either it may be\nsupposed, as is ordinarily done, that this something else is the\nabsolute orientation of the universe in space, or the rapidity with\nwhich this orientation varies; and this supposition may be correct; it\nis certainly the most convenient solution for geometry; it is not the\nmost satisfactory for the philosopher, because this orientation does not\nexist.\n\nOr it may be supposed that this something else is the position or the\nvelocity of some invisible body; this has been done by certain persons\nwho have even called it the body alpha, although we are doomed never to\nknow anything of this body but its name. This is an artifice entirely\nanalogous to that of which I spoke at the end of the paragraph devoted\nto my reflections on the principle of inertia.\n\nBut, after all, the difficulty is artificial. Provided the future\nindications of our instruments can depend only on the indications they\nhave given us or would have given us formerly, this is all that is\nnecessary. Now as to this we may rest easy.\n\n\n\n\nCHAPTER VIII\n\nENERGY AND THERMODYNAMICS\n\n\nENERGETICS.--The difficulties inherent in the classic mechanics have led\ncertain minds to prefer a new system they call _energetics_.\n\nEnergetics took its rise as an outcome of the discovery of the principle\nof the conservation of energy. Helmholtz gave it its final form.\n\nIt begins by defining two quantities which play the fundamental r\u00f4le in\nthis theory. They are _kinetic energy_, or _vis viva_, and _potential\nenergy_.\n\nAll the changes which bodies in nature can undergo are regulated by two\nexperimental laws:\n\n1\u00ba The sum of kinetic energy and potential energy is constant. This is\nthe principle of the conservation of energy.\n\n2\u00ba If a system of bodies is at _A_ at the time t_{0} and at _B_ at the\ntime t_{1}, it always goes from the first situation to the second in\nsuch a way that the _mean_ value of the difference between the two sorts\nof energy, in the interval of time which separates the two epochs t_{0}\nand t_{1}, may be as small as possible.\n\nThis is Hamilton's principle, which is one of the forms of the principle\nof least action.\n\nThe energetic theory has the following advantages over the classic\ntheory:\n\n1\u00ba It is less incomplete; that is to say, Hamilton's principle and that\nof the conservation of energy teach us more than the fundamental\nprinciples of the classic theory, and exclude certain motions not\nrealized in nature and which would be compatible with the classic\ntheory:\n\n2\u00ba It saves us the hypothesis of atoms, which it was almost impossible\nto avoid with the classic theory.\n\nBut it raises in its turn new difficulties:\n\nThe definitions of the two sorts of energy would raise difficulties\nalmost as great as those of force and mass in the first system. Yet\nthey may be gotten over more easily, at least in the simplest cases.\n\nSuppose an isolated system formed of a certain number of material\npoints; suppose these points subjected to forces depending only on their\nrelative position and their mutual distances, and independent of their\nvelocities. In virtue of the principle of the conservation of energy, a\nfunction of forces must exist.\n\nIn this simple case the enunciation of the principle of the conservation\nof energy is of extreme simplicity. A certain quantity, accessible to\nexperiment, must remain constant. This quantity is the sum of two terms;\nthe first depends only on the position of the material points and is\nindependent of their velocities; the second is proportional to the\nsquare of these velocities. This resolution can take place only in a\nsingle way.\n\nThe first of these terms, which I shall call _U_, will be the potential\nenergy; the second, which I shall call _T_, will be the kinetic energy.\n\nIt is true that if _T_ + _U_ is a constant, so is any function of _T_ +\n_U_,\n\n {Phi}(_T_ + _U_).\n\nBut this function {Phi}(_T_ + _U_) will not be the sum of two terms the\none independent of the velocities, the other proportional to the square\nof these velocities. Among the functions which remain constant there is\nonly one which enjoys this property, that is _T_ + _U_ (or a linear\nfunction of _T_ + _U_, which comes to the same thing, since this linear\nfunction may always be reduced to _T_ + _U_ by change of unit and of\norigin). This then is what we shall call energy; the first term we shall\ncall potential energy and the second kinetic energy. The definition of\nthe two sorts of energy can therefore be carried through without any\nambiguity.\n\nIt is the same with the definition of the masses. Kinetic energy, or\n_vis viva_, is expressed very simply by the aid of the masses and the\nrelative velocities of all the material points with reference to one of\nthem. These relative velocities are accessible to observation, and, when\nwe know the expression of the kinetic energy as function of these\nrelative velocities, the coefficients of this expression will give us\nthe masses.\n\nThus, in this simple case, the fundamental ideas may be defined without\ndifficulty. But the difficulties reappear in the more complicated cases\nand, for instance, if the forces, in lieu of depending only on the\ndistances, depend also on the velocities. For example, Weber supposes\nthe mutual action of two electric molecules to depend not only on their\ndistance, but on their velocity and their acceleration. If material\npoints should attract each other according to an analogous law, _U_\nwould depend on the velocity, and might contain a term proportional to\nthe square of the velocity.\n\nAmong the terms proportional to the squares of the velocities, how\ndistinguish those which come from _T_ or from _U_? Consequently, how\ndistinguish the two parts of energy?\n\nBut still more; how define energy itself? We no longer have any reason\nto take as definition _T_ + _U_ rather than any other function of _T_ +\n_U_, when the property which characterized _T_ + _U_ has disappeared,\nthat, namely, of being the sum of two terms of a particular form.\n\nBut this is not all; it is necessary to take account, not only of\nmechanical energy properly so called, but of the other forms of energy,\nheat, chemical energy, electric energy, etc. The principle of the\nconservation of energy should be written:\n\n _T_ + _U_ + _Q_ = const.\n\nwhere _T_ would represent the sensible kinetic energy, _U_ the potential\nenergy of position, depending only on the position of the bodies, _Q_\nthe internal molecular energy, under the thermal, chemic or electric\nform.\n\nAll would go well if these three terms were absolutely distinct, if _T_\nwere proportional to the square of the velocities, _U_ independent of\nthese velocities and of the state of the bodies, _Q_ independent of the\nvelocities and of the positions of the bodies and dependent only on\ntheir internal state.\n\nThe expression for the energy could be resolved only in one single way\ninto three terms of this form.\n\nBut this is not the case; consider electrified bodies; the electrostatic\nenergy due to their mutual action will evidently depend upon their\ncharge, that is to say, on their state; but it will equally depend upon\ntheir position. If these bodies are in motion, they will act one upon\nanother electrodynamically and the electrodynamic energy will depend not\nonly upon their state and their position, but upon their velocities.\n\nWe therefore no longer have any means of making the separation of the\nterms which should make part of _T_, of _U_ and of _Q_, and of\nseparating the three parts of energy.\n\nIf (_T_ + _U_ + _Q_) is constant so is any function [phi](_T_ + _U_ +\n_Q_).\n\nIf _T_ + _U_ + _Q_ were of the particular form I have above considered,\nno ambiguity would result; among the functions [phi](_T_ + _U_ + _Q_)\nwhich remain constant, there would only be one of this particular form,\nand that I should convene to call energy.\n\nBut as I have said, this is not rigorously the case; among the functions\nwhich remain constant, there is none which can be put rigorously under\nthis particular form; hence, how choose among them the one which should\nbe called energy? We no longer have anything to guide us in our choice.\n\nThere only remains for us one enunciation of the principle of the\nconservation of energy: _There is something which remains constant_.\nUnder this form it is in its turn out of the reach of experiment and\nreduces to a sort of tautology. It is clear that if the world is\ngoverned by laws, there will be quantities which will remain constant.\nLike Newton's laws, and, for an analogous reason, the principle of the\nconservation of energy, founded on experiment, could no longer be\ninvalidated by it.\n\nThis discussion shows that in passing from the classic to the energetic\nsystem progress has been made; but at the same time it shows this\nprogress is insufficient.\n\nAnother objection seems to me still more grave: the principle of least\naction is applicable to reversible phenomena; but it is not at all\nsatisfactory in so far as irreversible phenomena are concerned; the\nattempt by Helmholtz to extend it to this kind of phenomena did not\nsucceed and could not succeed; in this regard everything remains to be\ndone. The very statement of the principle of least action has something\nabout it repugnant to the mind. To go from one point to another, a\nmaterial molecule, acted upon by no force, but required to move on a\nsurface, will take the geodesic line, that is to say, the shortest\npath.\n\nThis molecule seems to know the point whither it is to go, to foresee\nthe time it would take to reach it by such and such a route, and then to\nchoose the most suitable path. The statement presents the molecule to\nus, so to speak, as a living and free being. Clearly it would be better\nto replace it by an enunciation less objectionable, and where, as the\nphilosophers would say, final causes would not seem to be substituted\nfor efficient causes.\n\nTHERMODYNAMICS.[4]--The r\u00f4le of the two fundamental principles of\nthermodynamics in all branches of natural philosophy becomes daily more\nimportant. Abandoning the ambitious theories of forty years ago, which\nwere encumbered by molecular hypotheses, we are trying to-day to erect\nupon thermodynamics alone the entire edifice of mathematical physics.\nWill the two principles of Mayer and of Clausius assure to it\nfoundations solid enough for it to last some time? No one doubts it; but\nwhence comes this confidence?\n\n [4] The following lines are a partial reproduction of the preface\n of my book _Thermodynamique_.\n\nAn eminent physicist said to me one day _\u00e0 propos_ of the law of errors:\n\"All the world believes it firmly, because the mathematicians imagine\nthat it is a fact of observation, and the observers that it is a theorem\nof mathematics.\" It was long so for the principle of the conservation of\nenergy. It is no longer so to-day; no one is ignorant that this is an\nexperimental fact.\n\nBut then what gives us the right to attribute to the principle itself\nmore generality and more precision than to the experiments which have\nserved to demonstrate it? This is to ask whether it is legitimate, as is\ndone every day, to generalize empirical data, and I shall not have the\npresumption to discuss this question, after so many philosophers have\nvainly striven to solve it. One thing is certain; if this power were\ndenied us, science could not exist or, at least, reduced to a sort of\ninventory, to the ascertaining of isolated facts, it would have no value\nfor us, since it could give no satisfaction to our craving for order and\nharmony and since it would be at the same time incapable of foreseeing.\nAs the circumstances which have preceded any fact will probably never be\nsimultaneously reproduced, a first generalization is already necessary\nto foresee whether this fact will be reproduced again after the least of\nthese circumstances shall be changed.\n\nBut every proposition may be generalized in an infinity of ways. Among\nall the generalizations possible, we must choose, and we can only choose\nthe simplest. We are therefore led to act as if a simple law were, other\nthings being equal, more probable than a complicated law.\n\nHalf a century ago this was frankly confessed, and it was proclaimed\nthat nature loves simplicity; she has since too often given us the lie.\nTo-day we no longer confess this tendency, and we retain only so much of\nit as is indispensable if science is not to become impossible.\n\nIn formulating a general, simple and precise law on the basis of\nexperiments relatively few and presenting certain divergences, we have\ntherefore only obeyed a necessity from which the human mind can not free\nitself.\n\nBut there is something more, and this is why I dwell upon the point.\n\nNo one doubts that Mayer's principle is destined to survive all the\nparticular laws from which it was obtained, just as Newton's law has\nsurvived Kepler's laws, from which it sprang, and which are only\napproximative if account be taken of perturbations.\n\nWhy does this principle occupy thus a sort of privileged place among all\nthe physical laws? There are many little reasons for it.\n\nFirst of all it is believed that we could not reject it or even doubt\nits absolute rigor without admitting the possibility of perpetual\nmotion; of course we are on our guard at such a prospect, and we think\nourselves less rash in affirming Mayer's principle than in denying it.\n\nThat is perhaps not wholly accurate; the impossibility of perpetual\nmotion implies the conservation of energy only for reversible phenomena.\n\nThe imposing simplicity of Mayer's principle likewise contributes to\nstrengthen our faith. In a law deduced immediately from experiment, like\nMariotte's, this simplicity would rather seem to us a reason for\ndistrust; but here this is no longer the case; we see elements, at first\nsight disparate, arrange themselves in an unexpected order and form a\nharmonious whole; and we refuse to believe that an unforeseen harmony\nmay be a simple effect of chance. It seems that our conquest is the\ndearer to us the more effort it has cost us, or that we are the surer of\nhaving wrested her true secret from nature the more jealously she has\nhidden it from us.\n\nBut those are only little reasons; to establish Mayer's law as an\nabsolute principle, a more profound discussion is necessary. But if this\nbe attempted, it is seen that this absolute principle is not even easy\nto state.\n\nIn each particular case it is clearly seen what energy is and at least a\nprovisional definition of it can be given; but it is impossible to find\na general definition for it.\n\nIf we try to enunciate the principle in all its generality and apply it\nto the universe, we see it vanish, so to speak, and nothing is left but\nthis: _There is something which remains constant_.\n\nBut has even this any meaning? In the determinist hypothesis, the state\nof the universe is determined by an extremely great number _n_ of\nparameters which I shall call x_{1}, x_{2},... x_{_n_}. As soon as\nthe values of these _n_ parameters at any instant are known, their\nderivatives with respect to the time are likewise known and consequently\nthe values of these same parameters at a preceding or subsequent instant\ncan be calculated. In other words, these _n_ parameters satisfy _n_\ndifferential equations of the first order.\n\nThese equations admit of _n_ - 1 integrals and consequently there are\n_n_ - 1 functions of x_{1}, x_{2},... x_{_n_}, which remain constant.\n_If then we say there is something which remains constant_, we only\nutter a tautology. We should even be puzzled to say which among all our\nintegrals should retain the name of energy.\n\nBesides, Mayer's principle is not understood in this sense when it is\napplied to a limited system. It is then assumed that _p_ of our\nparameters vary independently, so that we only have _n_ - _p_ relations,\ngenerally linear, between our _n_ parameters and their derivatives.\n\nTo simplify the enunciation, suppose that the sum of the work of the\nexternal forces is null, as well as that of the quantities of heat given\noff to the outside. Then the signification of our principle will be:\n\n_There is a combination of these n - p relations whose first member is\nan exact differential_; and then this differential vanishing in virtue\nof our _n_ - _p_ relations, its integral is a constant and this integral\nis called energy.\n\nBut how can it be possible that there are several parameters whose\nvariations are independent? That can only happen under the influence of\nexternal forces (although we have supposed, for simplicity, that the\nalgebraic sum of the effects of these forces is null). In fact, if the\nsystem were completely isolated from all external action, the values of\nour _n_ parameters at a given instant would suffice to determine the\nstate of the system at any subsequent instant, provided always we retain\nthe determinist hypothesis; we come back therefore to the same\ndifficulty as above.\n\nIf the future state of the system is not entirely determined by its\npresent state, this is because it depends besides upon the state of\nbodies external to the system. But then is it probable that there exist\nbetween the parameters _x_, which define the state of the system,\nequations independent of this state of the external bodies? and if in\ncertain cases we believe we can find such, is this not solely in\nconsequence of our ignorance and because the influence of these bodies\nis too slight for our experimenting to detect it?\n\nIf the system is not regarded as completely isolated, it is probable\nthat the rigorously exact expression of its internal energy will depend\non the state of the external bodies. Again, I have above supposed the\nsum of the external work was null, and if we try to free ourselves from\nthis rather artificial restriction, the enunciation becomes still more\ndifficult.\n\nTo formulate Mayer's principle in an absolute sense, it is therefore\nnecessary to extend it to the whole universe, and then we find ourselves\nface to face with the very difficulty we sought to avoid.\n\nIn conclusion, using ordinary language, the law of the conservation of\nenergy can have only one signification, which is that there is a\nproperty common to all the possibilities; but on the determinist\nhypothesis there is only a single possibility, and then the law has no\nlonger any meaning.\n\nOn the indeterminist hypothesis, on the contrary, it would have a\nmeaning, even if it were taken in an absolute sense; it would appear as\na limitation imposed upon freedom.\n\nBut this word reminds me that I am digressing and am on the point of\nleaving the domain of mathematics and physics. I check myself therefore\nand will stress of all this discussion only one impression, that Mayer's\nlaw is a form flexible enough for us to put into it almost whatever we\nwish. By that I do not mean it corresponds to no objective reality, nor\nthat it reduces itself to a mere tautology, since, in each particular\ncase, and provided one does not try to push to the absolute, it has a\nperfectly clear meaning.\n\nThis flexibility is a reason for believing in its permanence, and as, on\nthe other hand, it will disappear only to lose itself in a higher\nharmony, we may work with confidence, supporting ourselves upon it,\ncertain beforehand that our labor will not be lost.\n\nAlmost everything I have just said applies to the principle of Clausius.\nWhat distinguishes it is that it is expressed by an inequality. Perhaps\nit will be said it is the same with all physical laws, since their\nprecision is always limited by errors of observation. But they at least\nclaim to be first approximations, and it is hoped to replace them little\nby little by laws more and more precise. If, on the other hand, the\nprinciple of Clausius reduces to an inequality, this is not caused by\nthe imperfection of our means of observation, but by the very nature of\nthe question.\n\n\nGENERAL CONCLUSIONS ON PART THIRD\n\nThe principles of mechanics, then, present themselves to us under two\ndifferent aspects. On the one hand, they are truths founded on\nexperiment and approximately verified so far as concerns almost isolated\nsystems. On the other hand, they are postulates applicable to the\ntotality of the universe and regarded as rigorously true.\n\nIf these postulates possess a generality and a certainty which are\nlacking to the experimental verities whence they are drawn, this is\nbecause they reduce in the last analysis to a mere convention which we\nhave the right to make, because we are certain beforehand that no\nexperiment can ever contradict it.\n\nThis convention, however, is not absolutely arbitrary; it does not\nspring from our caprice; we adopt it because certain experiments have\nshown us that it would be convenient.\n\nThus is explained how experiment could make the principles of mechanics,\nand yet why it can not overturn them.\n\nCompare with geometry: The fundamental propositions of geometry, as for\ninstance Euclid's postulate, are nothing more than conventions, and it\nis just as unreasonable to inquire whether they are true or false as to\nask whether the metric system is true or false.\n\nOnly, these conventions are convenient, and it is certain experiments\nwhich have taught us that.\n\nAt first blush, the analogy is complete; the r\u00f4le of experiment seems\nthe same. One will therefore be tempted to say: Either mechanics must be\nregarded as an experimental science, and then the same must hold for\ngeometry; or else, on the contrary, geometry is a deductive science, and\nthen one may say as much of mechanics.\n\nSuch a conclusion would be illegitimate. The experiments which have led\nus to adopt as more convenient the fundamental conventions of geometry\nbear on objects which have nothing in common with those geometry\nstudies; they bear on the properties of solid bodies, on the rectilinear\npropagation of light. They are experiments of mechanics, experiments of\noptics; they can not in any way be regarded as experiments of geometry.\nAnd even the principal reason why our geometry seems convenient to us is\nthat the different parts of our body, our eye, our limbs, have the\nproperties of solid bodies. On this account, our fundamental experiments\nare preeminently physiological experiments, which bear, not on space\nwhich is the object the geometer must study, but on his body, that is\nto say, on the instrument he must use for this study.\n\nOn the contrary, the fundamental conventions of mechanics, and the\nexperiments which prove to us that they are convenient, bear on exactly\nthe same objects or on analogous objects. The conventional and general\nprinciples are the natural and direct generalization of the experimental\nand particular principles.\n\nLet it not be said that thus I trace artificial frontiers between the\nsciences; that if I separate by a barrier geometry properly so called\nfrom the study of solid bodies, I could just as well erect one between\nexperimental mechanics and the conventional mechanics of the general\nprinciples. In fact, who does not see that in separating these two\nsciences I mutilate them both, and that what will remain of conventional\nmechanics when it shall be isolated will be only a very small thing and\ncan in no way be compared to that superb body of doctrine called\ngeometry?\n\nOne sees now why the teaching of mechanics should remain experimental.\n\nOnly thus can it make us comprehend the genesis of the science, and that\nis indispensable for the complete understanding of the science itself.\n\nBesides, if we study mechanics, it is to apply it; and we can apply it\nonly if it remains objective. Now, as we have seen, what the principles\ngain in generality and certainty they lose in objectivity. It is,\ntherefore, above all with the objective side of the principles that we\nmust be familiarized early, and that can be done only by going from the\nparticular to the general, instead of the inverse.\n\nThe principles are conventions and disguised definitions. Yet they are\ndrawn from experimental laws; these laws have, so to speak, been exalted\ninto principles to which our mind attributes an absolute value.\n\nSome philosophers have generalized too far; they believed the principles\nwere the whole science and consequently that the whole science was\nconventional.\n\nThis paradoxical doctrine, called nominalism, will not bear\nexamination.\n\nHow can a law become a principle? It expressed a relation between two\nreal terms _A_ and _B_. But it was not rigorously true, it was only\napproximate. We introduce arbitrarily an intermediary term _C_ more or\nless fictitious, and _C_ is _by definition_ that which has with _A_\n_exactly_ the relation expressed by the law.\n\nThen our law is separated into an absolute and rigorous principle which\nexpresses the relation of _A_ to _C_ and an experimental law,\napproximate and subject to revision, which expresses the relation of _C_\nto _B_. It is clear that, however far this partition is pushed, some\nlaws will always be left remaining.\n\nWe go to enter now the domain of laws properly so called.\n\n\n\n\nPART IV\n\n\nNATURE\n\n\n\n\nCHAPTER IX\n\nHYPOTHESES IN PHYSICS\n\n\nTHE R\u00d4LE OF EXPERIMENT AND GENERALIZATION.--Experiment is the sole\nsource of truth. It alone can teach us anything new; it alone can give\nus certainty. These are two points that can not be questioned.\n\nBut then, if experiment is everything, what place will remain for\nmathematical physics? What has experimental physics to do with such an\naid, one which seems useless and perhaps even dangerous?\n\nAnd yet mathematical physics exists, and has done unquestionable\nservice. We have here a fact that must be explained.\n\nThe explanation is that merely to observe is not enough. We must use our\nobservations, and to do that we must generalize. This is what men always\nhave done; only as the memory of past errors has made them more and more\ncareful, they have observed more and more, and generalized less and\nless.\n\nEvery age has ridiculed the one before it, and accused it of having\ngeneralized too quickly and too na\u00efvely. Descartes pitied the Ionians;\nDescartes, in his turn, makes us smile. No doubt our children will some\nday laugh at us.\n\nBut can we not then pass over immediately to the goal? Is not this the\nmeans of escaping the ridicule that we foresee? Can we not be content\nwith just the bare experiment?\n\nNo, that is impossible; it would be to mistake utterly the true nature\nof science. The scientist must set in order. Science is built up with\nfacts, as a house is with stones. But a collection of facts is no more a\nscience than a heap of stones is a house.\n\nAnd above all the scientist must foresee. Carlyle has somewhere said\nsomething like this: \"Nothing but facts are of importance. John Lackland\npassed by here. Here is something that is admirable. Here is a reality\nfor which I would give all the theories in the world.\" Carlyle was a\nfellow countryman of Bacon; but Bacon would not have said that. That is\nthe language of the historian. The physicist would say rather: \"John\nLackland passed by here; that makes no difference to me, for he never\nwill pass this way again.\"\n\nWe all know that there are good experiments and poor ones. The latter\nwill accumulate in vain; though one may have made a hundred or a\nthousand, a single piece of work by a true master, by a Pasteur, for\nexample, will suffice to tumble them into oblivion. Bacon would have\nwell understood this; it is he who invented the phrase _Experimentum\ncrucis_. But Carlyle would not have understood it. A fact is a fact. A\npupil has read a certain number on his thermometer; he has taken no\nprecaution; no matter, he has read it, and if it is only the fact that\ncounts, here is a reality of the same rank as the peregrinations of King\nJohn Lackland. Why is the fact that this pupil has made this reading of\nno interest, while the fact that a skilled physicist had made another\nreading might be on the contrary very important? It is because from the\nfirst reading we could not infer anything. What then is a good\nexperiment? It is that which informs us of something besides an isolated\nfact; it is that which enables us to foresee, that is, that which\nenables us to generalize.\n\nFor without generalization foreknowledge is impossible. The\ncircumstances under which one has worked will never reproduce themselves\nall at once. The observed action then will never recur; the only thing\nthat can be affirmed is that under analogous circumstances an analogous\naction will be produced. In order to foresee, then, it is necessary to\ninvoke at least analogy, that is to say, already then to generalize.\n\nNo matter how timid one may be, still it is necessary to interpolate.\nExperiment gives us only a certain number of isolated points. We must\nunite these by a continuous line. This is a veritable generalization.\nBut we do more; the curve that we shall trace will pass between the\nobserved points and near these points; it will not pass through these\npoints themselves. Thus one does not restrict himself to generalizing\nthe experiments, but corrects them; and the physicist who should try to\nabstain from these corrections and really be content with the bare\nexperiment, would be forced to enunciate some very strange laws.\n\nThe bare facts, then, would not be enough for us; and that is why we\nmust have science ordered, or rather organized.\n\nIt is often said experiments must be made without a preconceived idea.\nThat is impossible. Not only would it make all experiment barren, but\nthat would be attempted which could not be done. Every one carries in\nhis mind his own conception of the world, of which he can not so easily\nrid himself. We must, for instance, use language; and our language is\nmade up only of preconceived ideas and can not be otherwise. Only these\nare unconscious preconceived ideas, a thousand times more dangerous than\nthe others.\n\nShall we say that if we introduce others, of which we are fully\nconscious, we shall only aggravate the evil? I think not. I believe\nrather that they will serve as counterbalances to each other--I was\ngoing to say as antidotes; they will in general accord ill with one\nanother--they will come into conflict with one another, and thereby\nforce us to regard things under different aspects. This is enough to\nemancipate us. He is no longer a slave who can choose his master.\n\nThus, thanks to generalization, each fact observed enables us to foresee\na great many others; only we must not forget that the first alone is\ncertain, that all others are merely probable. No matter how solidly\nfounded a prediction may appear to us, we are never _absolutely_ sure\nthat experiment will not contradict it, if we undertake to verify it.\nThe probability, however, is often so great that practically we may be\ncontent with it. It is far better to foresee even without certainty than\nnot to foresee at all.\n\nOne must, then, never disdain to make a verification when opportunity\noffers. But all experiment is long and difficult; the workers are few;\nand the number of facts that we need to foresee is immense. Compared\nwith this mass the number of direct verifications that we can make will\nnever be anything but a negligible quantity.\n\nOf this few that we can directly attain, we must make the best use; it\nis very necessary to get from every experiment the greatest possible\nnumber of predictions, and with the highest possible degree of\nprobability. The problem is, so to speak, to increase the yield of the\nscientific machine.\n\nLet us compare science to a library that ought to grow continually. The\nlibrarian has at his disposal for his purchases only insufficient funds.\nHe ought to make an effort not to waste them.\n\nIt is experimental physics that is entrusted with the purchases. It\nalone, then, can enrich the library.\n\nAs for mathematical physics, its task will be to make out the catalogue.\nIf the catalogue is well made, the library will not be any richer, but\nthe reader will be helped to use its riches.\n\nAnd even by showing the librarian the gaps in his collections, it will\nenable him to make a judicious use of his funds; which is all the more\nimportant because these funds are entirely inadequate.\n\nSuch, then, is the r\u00f4le of mathematical physics. It must direct\ngeneralization in such a manner as to increase what I just now called\nthe yield of science. By what means it can arrive at this, and how it\ncan do it without danger, is what remains for us to investigate.\n\nTHE UNITY OF NATURE.--Let us notice, first of all, that every\ngeneralization implies in some measure the belief in the unity and\nsimplicity of nature. As to the unity there can be no difficulty. If the\ndifferent parts of the universe were not like the members of one body,\nthey would not act on one another, they would know nothing of one\nanother; and we in particular would know only one of these parts. We do\nnot ask, then, if nature is one, but how it is one.\n\nAs for the second point, that is not such an easy matter. It is not\ncertain that nature is simple. Can we without danger act as if it were?\n\nThere was a time when the simplicity of Mariotte's law was an argument\ninvoked in favor of its accuracy; when Fresnel himself, after having\nsaid in a conversation with Laplace that nature was not concerned about\nanalytical difficulties, felt himself obliged to make explanations, in\norder not to strike too hard at prevailing opinion.\n\nTo-day ideas have greatly changed; and yet, those who do not believe\nthat natural laws have to be simple, are still often obliged to act as\nif they did. They could not entirely avoid this necessity without making\nimpossible all generalization, and consequently all science.\n\nIt is clear that any fact can be generalized in an infinity of ways, and\nit is a question of choice. The choice can be guided only by\nconsiderations of simplicity. Let us take the most commonplace case,\nthat of interpolation. We pass a continuous line, as regular as\npossible, between the points given by observation. Why do we avoid\npoints making angles and too abrupt turns? Why do we not make our curve\ndescribe the most capricious zig-zags? It is because we know beforehand,\nor believe we know, that the law to be expressed can not be so\ncomplicated as all that.\n\nWe may calculate the mass of Jupiter from either the movements of its\nsatellites, or the perturbations of the major planets, or those of the\nminor planets. If we take the averages of the determinations obtained by\nthese three methods, we find three numbers very close together, but\ndifferent. We might interpret this result by supposing that the\ncoefficient of gravitation is not the same in the three cases. The\nobservations would certainly be much better represented. Why do we\nreject this interpretation? Not because it is absurd, but because it is\nneedlessly complicated. We shall only accept it when we are forced to,\nand that is not yet.\n\nTo sum up, ordinarily every law is held to be simple till the contrary\nis proved.\n\nThis custom is imposed upon physicists by the causes that I have just\nexplained. But how shall we justify it in the presence of discoveries\nthat show us every day new details that are richer and more complex? How\nshall we even reconcile it with the belief in the unity of nature? For\nif everything depends on everything, relationships where so many diverse\nfactors enter can no longer be simple.\n\nIf we study the history of science, we see happen two inverse phenomena,\nso to speak. Sometimes simplicity hides under complex appearances;\nsometimes it is the simplicity which is apparent, and which disguises\nextremely complicated realities.\n\nWhat is more complicated than the confused movements of the planets?\nWhat simpler than Newton's law? Here nature, making sport, as Fresnel\nsaid, of analytical difficulties, employs only simple means, and by\ncombining them produces I know not what inextricable tangle. Here it is\nthe hidden simplicity which must be discovered.\n\nExamples of the opposite abound. In the kinetic theory of gases, one\ndeals with molecules moving with great velocities, whose paths, altered\nby incessant collisions, have the most capricious forms and traverse\nspace in every direction. The observable result is Mariotte's simple\nlaw. Every individual fact was complicated. The law of great numbers has\nreestablished simplicity in the average. Here the simplicity is merely\napparent, and only the coarseness of our senses prevents our perceiving\nthe complexity.\n\nMany phenomena obey a law of proportionality. But why? Because in these\nphenomena there is something very small. The simple law observed, then,\nis only a result of the general analytical rule that the infinitely\nsmall increment of a function is proportional to the increment of the\nvariable. As in reality our increments are not infinitely small, but\nvery small, the law of proportionality is only approximate, and the\nsimplicity is only apparent. What I have just said applies to the rule\nof the superposition of small motions, the use of which is so fruitful,\nand which is the basis of optics.\n\nAnd Newton's law itself? Its simplicity, so long undetected, is perhaps\nonly apparent. Who knows whether it is not due to some complicated\nmechanism, to the impact of some subtile matter animated by irregular\nmovements, and whether it has not become simple only through the action\nof averages and of great numbers? In any case, it is difficult not to\nsuppose that the true law contains complementary terms, which would\nbecome sensible at small distances. If in astronomy they are negligible\nas modifying Newton's law, and if the law thus regains its simplicity,\nit would be only because of the immensity of celestial distances.\n\nNo doubt, if our means of investigation should become more and more\npenetrating, we should discover the simple under the complex, then the\ncomplex under the simple, then again the simple under the complex, and\nso on, without our being able to foresee what will be the last term.\n\nWe must stop somewhere, and that science may be possible we must stop\nwhen we have found simplicity. This is the only ground on which we can\nrear the edifice of our generalizations. But this simplicity being only\napparent, will the ground be firm enough? This is what must be\ninvestigated.\n\nFor that purpose, let us see what part is played in our generalizations\nby the belief in simplicity. We have verified a simple law in a good\nmany particular cases; we refuse to admit that this agreement, so often\nrepeated, is simply the result of chance, and conclude that the law must\nbe true in the general case.\n\nKepler notices that a planet's positions, as observed by Tycho, are all\non one ellipse. Never for a moment does he have the thought that by a\nstrange play of chance Tycho never observed the heavens except at a\nmoment when the real orbit of the planet happened to cut this ellipse.\n\nWhat does it matter then whether the simplicity be real, or whether it\ncovers a complex reality? Whether it is due to the influence of great\nnumbers, which levels down individual differences, or to the greatness\nor smallness of certain quantities, which allows us to neglect certain\nterms, in no case is it due to chance. This simplicity, real or\napparent, always has a cause. We can always follow, then, the same\ncourse of reasoning, and if a simple law has been observed in several\nparticular cases, we can legitimately suppose that it will still be true\nin analogous cases. To refuse to do this would be to attribute to chance\nan inadmissible r\u00f4le.\n\nThere is, however, a difference. If the simplicity were real and\nessential, it would resist the increasing precision of our means of\nmeasure. If then we believe nature to be essentially simple, we must,\nfrom a simplicity that is approximate, infer a simplicity that is\nrigorous. This is what was done formerly; and this is what we no longer\nhave a right to do.\n\nThe simplicity of Kepler's laws, for example, is only apparent. That\ndoes not prevent their being applicable, very nearly, to all systems\nanalogous to the solar system; but it does prevent their being\nrigorously exact.\n\nTHE R\u00d4LE OF HYPOTHESIS.--All generalization is a hypothesis. Hypothesis,\nthen, has a necessary r\u00f4le that no one has ever contested. Only, it\nought always, as soon as possible and as often as possible, to be\nsubjected to verification. And, of course, if it does not stand this\ntest, it ought to be abandoned without reserve. This is what we\ngenerally do, but sometimes with rather an ill humor.\n\nWell, even this ill humor is not justified. The physicist who has just\nrenounced one of his hypotheses ought, on the contrary, to be full of\njoy; for he has found an unexpected opportunity for discovery. His\nhypothesis, I imagine, had not been adopted without consideration; it\ntook account of all the known factors that it seemed could enter into\nthe phenomenon. If the test does not support it, it is because there is\nsomething unexpected and extraordinary; and because there is going to be\nsomething found that is unknown and new.\n\nHas the discarded hypothesis, then, been barren? Far from that, it may\nbe said it has rendered more service than a true hypothesis. Not only\nhas it been the occasion of the decisive experiment, but, without having\nmade the hypothesis, the experiment would have been made by chance, so\nthat nothing would have been derived from it. One would have seen\nnothing extraordinary; only one fact the more would have been catalogued\nwithout deducing from it the least consequence.\n\nNow on what condition is the use of hypothesis without danger?\n\nThe firm determination to submit to experiment is not enough; there are\nstill dangerous hypotheses; first, and above all, those which are tacit\nand unconscious. Since we make them without knowing it, we are powerless\nto abandon them. Here again, then, is a service that mathematical\nphysics can render us. By the precision that is characteristic of it, it\ncompels us to formulate all the hypotheses that we should make without\nit, but unconsciously.\n\nLet us notice besides that it is important not to multiply hypotheses\nbeyond measure, and to make them only one after the other. If we\nconstruct a theory based on a number of hypotheses, and if experiment\ncondemns it, which of our premises is it necessary to change? It will be\nimpossible to know. And inversely, if the experiment succeeds, shall we\nbelieve that we have demonstrated all the hypotheses at once? Shall we\nbelieve that with one single equation we have determined several\nunknowns?\n\nWe must equally take care to distinguish between the different kinds of\nhypotheses. There are first those which are perfectly natural and from\nwhich one can scarcely escape. It is difficult not to suppose that the\ninfluence of bodies very remote is quite negligible, that small\nmovements follow a linear law, that the effect is a continuous function\nof its cause. I will say as much of the conditions imposed by symmetry.\nAll these hypotheses form, as it were, the common basis of all the\ntheories of mathematical physics. They are the last that ought to be\nabandoned.\n\nThere is a second class of hypotheses, that I shall term neutral. In\nmost questions the analyst assumes at the beginning of his calculations\neither that matter is continuous or, on the contrary, that it is formed\nof atoms. He might have made the opposite assumption without changing\nhis results. He would only have had more trouble to obtain them; that is\nall. If, then, experiment confirms his conclusions, will he think that\nhe has demonstrated, for instance, the real existence of atoms?\n\nIn optical theories two vectors are introduced, of which one is regarded\nas a velocity, the other as a vortex. Here again is a neutral\nhypothesis, since the same conclusions would have been reached by taking\nprecisely the opposite. The success of the experiment, then, can not\nprove that the first vector is indeed a velocity; it can only prove one\nthing, that it is a vector. This is the only hypothesis that has really\nbeen introduced in the premises. In order to give it that concrete\nappearance which the weakness of our minds requires, it has been\nnecessary to consider it either as a velocity or as a vortex, in the\nsame way that it has been necessary to represent it by a letter, either\n_x_ or _y_. The result, however, whatever it may be, will not prove that\nit was right or wrong to regard it as a velocity any more than it will\nprove that it was right or wrong to call it _x_ and not _y_.\n\nThese neutral hypotheses are never dangerous, if only their character is\nnot misunderstood. They may be useful, either as devices for\ncomputation, or to aid our understanding by concrete images, to fix our\nideas as the saying is. There is, then, no occasion to exclude them.\n\nThe hypotheses of the third class are the real generalizations. They are\nthe ones that experiment must confirm or invalidate. Whether verified or\ncondemned, they will always be fruitful. But for the reasons that I have\nset forth, they will only be fruitful if they are not too numerous.\n\nORIGIN OF MATHEMATICAL PHYSICS.--Let us penetrate further, and study\nmore closely the conditions that have permitted the development of\nmathematical physics. We observe at once that the efforts of scientists\nhave always aimed to resolve the complex phenomenon directly given by\nexperiment into a very large number of elementary phenomena.\n\nThis is done in three different ways: first, in time. Instead of\nembracing in its entirety the progressive development of a phenomenon,\nthe aim is simply to connect each instant with the instant immediately\npreceding it. It is admitted that the actual state of the world depends\nonly on the immediate past, without being directly influenced, so to\nspeak, by the memory of a distant past. Thanks to this postulate,\ninstead of studying directly the whole succession of phenomena, it is\npossible to confine ourselves to writing its 'differential equation.'\nFor Kepler's laws we substitute Newton's law.\n\nNext we try to analyze the phenomenon in space. What experiment gives us\nis a confused mass of facts presented on a stage of considerable extent.\nWe must try to discover the elementary phenomenon, which will be, on the\ncontrary, localized in a very small region of space.\n\nSome examples will perhaps make my thought better understood. If we\nwished to study in all its complexity the distribution of temperature in\na cooling solid, we should never succeed. Everything becomes simple if\nwe reflect that one point of the solid can not give up its heat directly\nto a distant point; it will give up its heat only to the points in the\nimmediate neighborhood, and it is by degrees that the flow of heat can\nreach other parts of the solid. The elementary phenomenon is the\nexchange of heat between two contiguous points. It is strictly\nlocalized, and is relatively simple, if we admit, as is natural, that it\nis not influenced by the temperature of molecules whose distance is\nsensible.\n\nI bend a rod. It is going to take a very complicated form, the direct\nstudy of which would be impossible. But I shall be able, however, to\nattack it, if I observe that its flexure is a result only of the\ndeformation of the very small elements of the rod, and that the\ndeformation of each of these elements depends only on the forces that\nare directly applied to it, and not at all on those which may act on the\nother elements.\n\nIn all these examples, which I might easily multiply, we admit that\nthere is no action at a distance, or at least at a great distance. This\nis a hypothesis. It is not always true, as the law of gravitation shows\nus. It must, then, be submitted to verification. If it is confirmed,\neven approximately, it is precious, for it will enable us to make\nmathematical physics, at least by successive approximations.\n\nIf it does not stand the test, we must look for something else\nanalogous; for there are still other means of arriving at the elementary\nphenomenon. If several bodies act simultaneously, it may happen that\ntheir actions are independent and are simply added to one another,\neither as vectors or as scalars. The elementary phenomenon is then the\naction of an isolated body. Or again, we have to deal with small\nmovements, or more generally with small variations, which obey the\nwell-known law of superposition. The observed movement will then be\ndecomposed into simple movements, for example, sound into its harmonics,\nwhite light into its monochromatic components.\n\nWhen we have discovered in what direction it is advisable to look for\nthe elementary phenomenon, by what means can we reach it?\n\nFirst of all, it will often happen that in order to detect it, or rather\nto detect the part of it useful to us, it will not be necessary to\npenetrate the mechanism; the law of great numbers will suffice.\n\nLet us take again the instance of the propagation of heat. Every\nmolecule emits rays toward every neighboring molecule. According to what\nlaw, we do not need to know. If we should make any supposition in regard\nto this, it would be a neutral hypothesis and consequently useless and\nincapable of verification. And, in fact, by the action of averages and\nthanks to the symmetry of the medium, all the differences are leveled\ndown, and whatever hypothesis may be made, the result is always the\nsame.\n\nThe same circumstance is presented in the theory of electricity and in\nthat of capillarity. The neighboring molecules attract and repel one\nanother. We do not need to know according to what law; it is enough for\nus that this attraction is sensible only at small distances, and that\nthe molecules are very numerous, that the medium is symmetrical, and we\nshall only have to let the law of great numbers act.\n\nHere again the simplicity of the elementary phenomenon was hidden under\nthe complexity of the resultant observable phenomenon; but, in its turn,\nthis simplicity was only apparent, and concealed a very complex\nmechanism.\n\nThe best means of arriving at the elementary phenomenon would evidently\nbe experiment. We ought by experimental contrivance to dissociate the\ncomplex sheaf that nature offers to our researches, and to study with\ncare the elements as much isolated as possible. For example, natural\nwhite light would be decomposed into monochromatic lights by the aid of\nthe prism, and into polarized light by the aid of the polarizer.\n\nUnfortunately that is neither always possible nor always sufficient, and\nsometimes the mind must outstrip experiment. I shall cite only one\nexample, which has always struck me forcibly.\n\nIf I decompose white light, I shall be able to isolate a small part of\nthe spectrum, but however small it may be, it will retain a certain\nbreadth. Likewise the natural lights, called _monochromatic_, give us a\nvery narrow line, but not, however, infinitely narrow. It might be\nsupposed that by studying experimentally the properties of these natural\nlights, by working with finer and finer lines of the spectrum, and by\npassing at last to the limit, so to speak, we should succeed in learning\nthe properties of a light strictly monochromatic.\n\nThat would not be accurate. Suppose that two rays emanate from the same\nsource, that we polarize them first in two perpendicular planes, then\nbring them back to the same plane of polarization, and try to make them\ninterfere. If the light were _strictly_ monochromatic, they would\ninterfere. With our lights, which are nearly monochromatic, there will\nbe no interference, and that no matter how narrow the line. In order to\nbe otherwise it would have to be several million times as narrow as the\nfinest known lines.\n\nHere, then, the passage to the limit would have deceived us. The mind\nmust outstrip the experiment, and if it has done so with success, it is\nbecause it has allowed itself to be guided by the instinct of\nsimplicity.\n\nThe knowledge of the elementary fact enables us to put the problem in an\nequation. Nothing remains but to deduce from this by combination the\ncomplex fact that can be observed and verified. This is what is called\n_integration_, and is the business of the mathematician.\n\nIt may be asked why, in physical sciences, generalization so readily\ntakes the mathematical form. The reason is now easy to see. It is not\nonly because we have numerical laws to express; it is because the\nobservable phenomenon is due to the superposition of a great number of\nelementary phenomena _all alike_. Thus quite naturally are introduced\ndifferential equations.\n\nIt is not enough that each elementary phenomenon obeys simple laws; all\nthose to be combined must obey the same law. Then only can the\nintervention of mathematics be of use; mathematics teaches us in fact to\ncombine like with like. Its aim is to learn the result of a combination\nwithout needing to go over the combination piece by piece. If we have to\nrepeat several times the same operation, it enables us to avoid this\nrepetition by telling us in advance the result of it by a sort of\ninduction. I have explained this above, in the chapter on mathematical\nreasoning.\n\nBut for this, all the operations must be alike. In the opposite case, it\nwould evidently be necessary to resign ourselves to doing them in\nreality one after another, and mathematics would become useless.\n\nIt is then thanks to the approximate homogeneity of the matter studied\nby physicists that mathematical physics could be born.\n\nIn the natural sciences, we no longer find these conditions:\nhomogeneity, relative independence of remote parts, simplicity of the\nelementary fact; and this is why naturalists are obliged to resort to\nother methods of generalization.\n\n\n\n\nCHAPTER X\n\nTHE THEORIES OF MODERN PHYSICS\n\n\nMEANING OF PHYSICAL THEORIES.--The laity are struck to see how ephemeral\nscientific theories are. After some years of prosperity, they see them\nsuccessively abandoned; they see ruins accumulate upon ruins; they\nforesee that the theories fashionable to-day will shortly succumb in\ntheir turn and hence they conclude that these are absolutely idle. This\nis what they call the _bankruptcy of science_.\n\nTheir skepticism is superficial; they give no account to themselves of\nthe aim and the r\u00f4le of scientific theories; otherwise they would\ncomprehend that the ruins may still be good for something.\n\nNo theory seemed more solid than that of Fresnel which attributed light\nto motions of the ether. Yet now Maxwell's is preferred. Does this mean\nthe work of Fresnel was in vain? No, because the aim of Fresnel was not\nto find out whether there is really an ether, whether it is or is not\nformed of atoms, whether these atoms really move in this or that sense;\nhis object was to foresee optical phenomena.\n\nNow, Fresnel's theory always permits of this, to-day as well as before\nMaxwell. The differential equations are always true; they can always be\nintegrated by the same procedures and the results of this integration\nalways retain their value.\n\nAnd let no one say that thus we reduce physical theories to the r\u00f4le of\nmere practical recipes; these equations express relations, and if the\nequations remain true it is because these relations preserve their\nreality. They teach us, now as then, that there is such and such a\nrelation between some thing and some other thing; only this something\nformerly we called _motion_; we now call it _electric current_. But\nthese appellations were only images substituted for the real objects\nwhich nature will eternally hide from us. The true relations between\nthese real objects are the only reality we can attain to, and the only\ncondition is that the same relations exist between these objects as\nbetween the images by which we are forced to replace them. If these\nrelations are known to us, what matter if we deem it convenient to\nreplace one image by another.\n\nThat some periodic phenomenon (an electric oscillation, for instance) is\nreally due to the vibration of some atom which, acting like a pendulum,\nreally moves in this or that sense, is neither certain nor interesting.\nBut that between electric oscillation, the motion of the pendulum and\nall periodic phenomena there exists a close relationship which\ncorresponds to a profound reality; that this relationship, this\nsimilitude, or rather this parallelism extends into details; that it is\na consequence of more general principles, that of energy and that of\nleast action; this is what we can affirm; this is the truth which will\nalways remain the same under all the costumes in which we may deem it\nuseful to deck it out.\n\nNumerous theories of dispersion have been proposed; the first was\nimperfect and contained only a small part of truth. Afterwards came that\nof Helmholtz; then it was modified in various ways, and its author\nhimself imagined another founded on the principles of Maxwell. But, what\nis remarkable, all the scientists who came after Helmholtz reached the\nsame equations, starting from points of departure in appearance very\nwidely separated. I will venture to say these theories are all true at\nthe same time, not only because they make us foresee the same phenomena,\nbut because they put in evidence a true relation, that of absorption and\nanomalous dispersion. What is true in the premises of these theories is\nwhat is common to all the authors; this is the affirmation of this or\nthat relation between certain things which some call by one name, others\nby another.\n\nThe kinetic theory of gases has given rise to many objections, which we\ncould hardly answer if we pretended to see in it the absolute truth. But\nall these objections will not preclude its having been useful, and\nparticularly so in revealing to us a relation true and but for it\nprofoundly hidden, that of the gaseous pressure and the osmotic\npressure. In this sense, then, it may be said to be true.\n\nWhen a physicist finds a contradiction between two theories equally\ndear to him, he sometimes says: \"We will not bother about that, but hold\nfirmly the two ends of the chain, though the intermediate links are\nhidden from us.\" This argument of an embarrassed theologian would be\nridiculous if it were necessary to attribute to physical theories the\nsense the laity give them. In case of contradiction, one of them at\nleast must then be regarded as false. It is no longer the same if in\nthem be sought only what should be sought. May be they both express true\nrelations and the contradiction is only in the images wherewith we have\nclothed the reality.\n\nTo those who find we restrict too much the domain accessible to the\nscientist, I answer: These questions which we interdict to you and which\nyou regret, are not only insoluble, they are illusory and devoid of\nmeaning.\n\nSome philosopher pretends that all physics may be explained by the\nmutual impacts of atoms. If he merely means there are between physical\nphenomena the same relations as between the mutual impacts of a great\nnumber of balls, well and good, that is verifiable, that is perhaps\ntrue. But he means something more; and we think we understand it because\nwe think we know what impact is in itself; why? Simply because we have\noften seen games of billiards. Shall we think God, contemplating his\nwork, feels the same sensations as we in watching a billiard match? If\nwe do not wish to give this bizarre sense to his assertion, if neither\ndo we wish the restricted sense I have just explained, which is good\nsense, then it has none.\n\nHypotheses of this sort have therefore only a metaphorical sense. The\nscientist should no more interdict them than the poet does metaphors;\nbut he ought to know what they are worth. They may be useful to give a\ncertain satisfaction to the mind, and they will not be injurious\nprovided they are only indifferent hypotheses.\n\nThese considerations explain to us why certain theories, supposed to be\nabandoned and finally condemned by experiment, suddenly arise from their\nashes and recommence a new life. It is because they expressed true\nrelations; and because they had not ceased to do so when, for one reason\nor another, we felt it necessary to enunciate the same relations in\nanother language. So they retained a sort of latent life.\n\nScarcely fifteen years ago was there anything more ridiculous, more\nna\u00efvely antiquated, than Coulomb's fluids? And yet here they are\nreappearing under the name of _electrons_. Wherein do these permanently\nelectrified molecules differ from Coulomb's electric molecules? It is\ntrue that in the electrons the electricity is supported by a little, a\nvery little matter; in other words, they have a mass (and yet this is\nnow contested); but Coulomb did not deny mass to his fluids, or, if he\ndid, it was only with reluctance. It would be rash to affirm that the\nbelief in electrons will not again suffer eclipse; it was none the less\ncurious to note this unexpected resurrection.\n\nBut the most striking example is Carnot's principle. Carnot set it up\nstarting from false hypotheses; when it was seen that heat is not\nindestructible, but may be transformed into work, his ideas were\ncompletely abandoned; afterwards Clausius returned to them and made them\nfinally triumph. Carnot's theory, under its primitive form, expressed,\naside from true relations, other inexact relations, _d\u00e9bris_ of\nantiquated ideas; but the presence of these latter did not change the\nreality of the others. Clausius had only to discard them as one lops off\ndead branches.\n\nThe result was the second fundamental law of thermodynamics. There were\nalways the same relations; though these relations no longer subsisted,\nat least in appearance, between the same objects. This was enough for\nthe principle to retain its value. And even the reasonings of Carnot\nhave not perished because of that; they were applied to a material\ntainted with error; but their form (that is to say, the essential)\nremained correct.\n\nWhat I have just said illuminates at the same time the r\u00f4le of general\nprinciples such as the principle of least action, or that of the\nconservation of energy.\n\nThese principles have a very high value; they were obtained in seeking\nwhat there was in common in the enunciation of numerous physical laws;\nthey represent therefore, as it were, the quintessence of innumerable\nobservations.\n\nHowever, from their very generality a consequence results to which I\nhave called attention in Chapter VIII, namely, that they can no longer\nbe verified. As we can not give a general definition of energy, the\nprinciple of the conservation of energy signifies simply that there is\n_something_ which remains constant. Well, whatever be the new notions\nthat future experiments shall give us about the world, we are sure in\nadvance that there will be something there which will remain constant\nand which may be called _energy_.\n\nIs this to say that the principle has no meaning and vanishes in a\ntautology? Not at all; it signifies that the different things to which\nwe give the name of _energy_ are connected by a true kinship; it affirms\na real relation between them. But then if this principle has a meaning,\nit may be false; it may be that we have not the right to extend\nindefinitely its applications, and yet it is certain beforehand to be\nverified in the strict acceptation of the term; how then shall we know\nwhen it shall have attained all the extension which can legitimately be\ngiven it? Just simply when it shall cease to be useful to us, that is,\nto make us correctly foresee new phenomena. We shall be sure in such a\ncase that the relation affirmed is no longer real; for otherwise it\nwould be fruitful; experiment, without directly contradicting a new\nextension of the principle, will yet have condemned it.\n\nPHYSICS AND MECHANISM.--Most theorists have a constant predilection for\nexplanations borrowed from mechanics or dynamics. Some would be\nsatisfied if they could explain all phenomena by motions of molecules\nattracting each other according to certain laws. Others are more\nexacting; they would suppress attractions at a distance; their molecules\nshould follow rectilinear paths from which they could be made to deviate\nonly by impacts. Others again, like Hertz, suppress forces also, but\nsuppose their molecules subjected to geometric attachments analogous,\nfor instance, to those of our linkages; they try thus to reduce dynamics\nto a sort of kinematics.\n\nIn a word, all would bend nature into a certain form outside of which\ntheir mind could not feel satisfied. Will nature be sufficiently\nflexible for that?\n\nWe shall examine this question in Chapter XII, _\u00e0 propos_ of Maxwell's\ntheory. Whenever the principles of energy and of least action are\nsatisfied, we shall see not only that there is always one possible\nmechanical explanation, but that there is always an infinity of them.\nThanks to a well-known theorem of K\u00f6nig's on linkages, it could be\nshown that we can, in an infinity of ways, explain everything by\nattachments after the manner of Hertz, or also by central forces.\nWithout doubt it could be demonstrated just as easily that everything\ncan always be explained by simple impacts.\n\nFor that, of course, we need not be content with ordinary matter, with\nthat which falls under our senses and whose motions we observe directly.\nEither we shall suppose that this common matter is formed of atoms whose\ninternal motions elude us, the displacement of the totality alone\nremaining accessible to our senses. Or else we shall imagine some one of\nthose subtile fluids which under the name of _ether_ or under other\nnames, have at all times played so great a r\u00f4le in physical theories.\n\nOften one goes further and regards the ether as the sole primitive\nmatter or even as the only true matter. The more moderate consider\ncommon matter as condensed ether, which is nothing startling; but others\nreduce still further its importance and see in it nothing more than the\ngeometric locus of the ether's singularities. For instance, what we call\n_matter_ is for Lord Kelvin only the locus of points where the ether is\nanimated by vortex motions; for Riemann, it was the locus of points\nwhere ether is constantly destroyed; for other more recent authors,\nWiechert or Larmor, it is the locus of points where the ether undergoes\na sort of torsion of a very particular nature. If the attempt is made to\noccupy one of these points of view, I ask myself by what right shall we\nextend to the ether, under pretext that this is the true matter,\nmechanical properties observed in ordinary matter, which is only false\nmatter.\n\nThe ancient fluids, caloric, electricity, etc., were abandoned when it\nwas perceived that heat is not indestructible. But they were abandoned\nfor another reason also. In materializing them, their individuality was,\nso to speak, emphasized, a sort of abyss was opened between them. This\nhad to be filled up on the coming of a more vivid feeling of the unity\nof nature, and the perception of the intimate relations which bind\ntogether all its parts. Not only did the old physicists, in multiplying\nfluids, create entities unnecessarily, but they broke real ties.\n\nIt is not sufficient for a theory to affirm no false relations, it must\nnot hide true relations.\n\nAnd does our ether really exist? We know the origin of our belief in the\nether. If light reaches us from a distant star, during several years it\nwas no longer on the star and not yet on the earth; it must then be\nsomewhere and sustained, so to speak, by some material support.\n\nThe same idea may be expressed under a more mathematical and more\nabstract form. What we ascertain are the changes undergone by material\nmolecules; we see, for instance, that our photographic plate feels the\nconsequences of phenomena of which the incandescent mass of the star was\nthe theater several years before. Now, in ordinary mechanics the state\nof the system studied depends only on its state at an instant\nimmediately anterior; therefore the system satisfies differential\nequations. On the contrary, if we should not believe in the ether, the\nstate of the material universe would depend not only on the state\nimmediately preceding, but on states much older; the system would\nsatisfy equations of finite differences. It is to escape this derogation\nof the general laws of mechanics that we have invented the ether.\n\nThat would still only oblige us to fill up, with the ether, the\ninterplanetary void, but not to make it penetrate the bosom of the\nmaterial media themselves. Fizeau's experiment goes further. By the\ninterference of rays which have traversed air or water in motion, it\nseems to show us two different media interpenetrating and yet changing\nplace one with regard to the other.\n\nWe seem to touch the ether with the finger.\n\nYet experiments may be conceived which would make us touch it still more\nnearly. Suppose Newton's principle, of the equality of action and\nreaction, no longer true if applied to matter _alone_, and that we have\nestablished it. The geometric sum of all the forces applied to all the\nmaterial molecules would no longer be null. It would be necessary then,\nif we did not wish to change all mechanics, to introduce the ether, in\norder that this action which matter appeared to experience should be\ncounterbalanced by the reaction of matter on something.\n\nOr again, suppose we discover that optical and electrical phenomena are\ninfluenced by the motion of the earth. We should be led to conclude that\nthese phenomena might reveal to us not only the relative motions of\nmaterial bodies, but what would seem to be their absolute motions.\nAgain, an ether would be necessary, that these so-called absolute\nmotions should not be their displacements with regard to a void space,\nbut their displacements with regard to something concrete.\n\nShall we ever arrive at that? I have not this hope, I shall soon say\nwhy, and yet it is not so absurd, since others have had it.\n\nFor instance, if the theory of Lorentz, of which I shall speak in detail\nfurther on in Chapter XIII., were true, Newton's principle would not\napply to matter _alone_, and the difference would not be very far from\nbeing accessible to experiment.\n\nOn the other hand, many researches have been made on the influence of\nthe earth's motion. The results have always been negative. But these\nexperiments were undertaken because the outcome was not sure in advance,\nand, indeed, according to the ruling theories, the compensation would be\nonly approximate, and one might expect to see precise methods give\npositive results.\n\nI believe that such a hope is illusory; it was none the less interesting\nto show that a success of this sort would open to us, in some sort, a\nnew world.\n\nAnd now I must be permitted a digression; I must explain, in fact, why I\ndo not believe, despite Lorentz, that more precise observations can ever\nput in evidence anything else than the relative displacements of\nmaterial bodies. Experiments have been made which should have disclosed\nthe terms of the first order; the results have been negative; could that\nbe by chance? No one has assumed that; a general explanation has been\nsought, and Lorentz has found it; he has shown that the terms of the\nfirst order must destroy each other, but not those of the second. Then\nmore precise experiments were made; they also were negative; neither\ncould this be the effect of chance; an explanation was necessary; it was\nfound; they always are found; of hypotheses there is never lack.\n\nBut this is not enough; who does not feel that this is still to leave to\nchance too great a r\u00f4le? Would not that also be a chance, this singular\ncoincidence which brought it about that a certain circumstance should\ncome just in the nick of time to destroy the terms of the first order,\nand that another circumstance, wholly different, but just as opportune,\nshould take upon itself to destroy those of the second order? No, it is\nnecessary to find an explanation the same for the one as for the other,\nand then everything leads us to think that this explanation will hold\ngood equally well for the terms of higher order, and that the mutual\ndestruction of these terms will be rigorous and absolute.\n\nPRESENT STATE OF THE SCIENCE.--In the history of the development of\nphysics we distinguish two inverse tendencies.\n\nOn the one hand, new bonds are continually being discovered between\nobjects which had seemed destined to remain forever unconnected;\nscattered facts cease to be strangers to one another; they tend to\narrange themselves in an imposing synthesis. Science advances toward\nunity and simplicity.\n\nOn the other hand, observation reveals to us every day new phenomena;\nthey must long await their place and sometimes, to make one for them, a\ncorner of the edifice must be demolished. In the known phenomena\nthemselves, where our crude senses showed us uniformity, we perceive\ndetails from day to day more varied; what we believed simple becomes\ncomplex, and science appears to advance toward variety and complexity.\n\nOf these two inverse tendencies, which seem to triumph turn about, which\nwill win? If it be the first, science is possible; but nothing proves\nthis _a priori_, and it may well be feared that after having made vain\nefforts to bend nature in spite of herself to our ideal of unity,\nsubmerged by the ever-rising flood of our new riches, we must renounce\nclassifying them, abandon our ideal, and reduce science to the\nregistration of innumerable recipes.\n\nTo this question we can not reply. All we can do is to observe the\nscience of to-day and compare it with that of yesterday. From this\nexamination we may doubtless draw some encouragement.\n\nHalf a century ago, hope ran high. The discovery of the conservation of\nenergy and of its transformations had revealed to us the unity of force.\nThus it showed that the phenomena of heat could be explained by\nmolecular motions. What was the nature of these motions was not exactly\nknown, but no one doubted that it soon would be. For light, the task\nseemed completely accomplished. In what concerns electricity, things\nwere less advanced. Electricity had just annexed magnetism. This was a\nconsiderable step toward unity, and a decisive step.\n\nBut how should electricity in its turn enter into the general unity, how\nshould it be reduced to the universal mechanism?\n\nOf that no one had any idea. Yet the possibility of this reduction was\ndoubted by none, there was faith. Finally, in what concerns the\nmolecular properties of material bodies, the reduction seemed still\neasier, but all the detail remained hazy. In a word, the hopes were vast\nand animated, but vague. To-day, what do we see? First of all, a prime\nprogress, immense progress. The relations of electricity and light are\nnow known; the three realms, of light, of electricity and of magnetism,\npreviously separated, form now but one; and this annexation seems final.\n\nThis conquest, however, has cost us some sacrifices. The optical\nphenomena subordinate themselves as particular cases under the\nelectrical phenomena; so long as they remained isolated, it was easy to\nexplain them by motions that were supposed to be known in all their\ndetails, that was a matter of course; but now an explanation, to be\nacceptable, must be easily capable of extension to the entire electric\ndomain. Now that is a matter not without difficulties.\n\nThe most satisfactory theory we have is that of Lorentz, which, as we\nshall see in the last chapter, explains electric currents by the motions\nof little electrified particles; it is unquestionably the one which best\nexplains the known facts, the one which illuminates the greatest number\nof true relations, the one of which most traces will be found in the\nfinal construction. Nevertheless, it still has a serious defect, which I\nhave indicated above; it is contrary to Newton's law of the equality of\naction and reaction; or rather, this principle, in the eyes of Lorentz,\nwould not be applicable to matter alone; for it to be true, it would be\nnecessary to take account of the action of the ether on matter and of\nthe reaction of matter on the ether.\n\nNow, from what we know at present, it seems probable that things do not\nhappen in this way.\n\nHowever that may be, thanks to Lorentz, Fizeau's results on the optics\nof moving bodies, the laws of normal and anomalous dispersion and of\nabsorption find themselves linked to one another and to the other\nproperties of the ether by bonds which beyond any doubt will never more\nbe broken. See the facility with which the new Zeeman effect has found\nits place already and has even aided in classifying Faraday's magnetic\nrotation which had defied Maxwell's efforts; this facility abundantly\nproves that the theory of Lorentz is not an artificial assemblage\ndestined to fall asunder. It will probably have to be modified, but not\ndestroyed.\n\nBut Lorentz had no aim beyond that of embracing in one totality all the\noptics and electrodynamics of moving bodies; he never pretended to give\na mechanical explanation of them. Larmor goes further; retaining the\ntheory of Lorentz in essentials, he grafts upon it, so to speak,\nMacCullagh's ideas on the direction of the motions of the ether.\n\nAccording to him, the velocity of the ether would have the same\ndirection and the same magnitude as the magnetic force. However\ningenious this attempt may be, the defect of the theory of Lorentz\nremains and is even aggravated. With Lorentz, we do not know what are\nthe motions of the ether; thanks to this ignorance, we may suppose them\nsuch that, compensating those of matter, they reestablish the equality\nof action and reaction. With Larmor, we know the motions of the ether,\nand we can ascertain that the compensation does not take place.\n\nIf Larmor has failed, as it seems to me he has, does that mean that a\nmechanical explanation is impossible? Far from it: I have said above\nthat when a phenomenon obeys the two principles of energy and of least\naction, it admits of an infinity of mechanical explanations; so it is,\ntherefore, with the optical and electrical phenomena.\n\nBut this is not enough: for a mechanical explanation to be good, it must\nbe simple; for choosing it among all which are possible, there should be\nother reasons besides the necessity of making a choice. Well, we have\nnot as yet a theory satisfying this condition and consequently good for\nsomething. Must we lament this? That would be to forget what is the goal\nsought; this is not mechanism; the true, the sole aim is unity.\n\nWe must therefore set bounds to our ambition; let us not try to\nformulate a mechanical explanation; let us be content with showing that\nwe could always find one if we wished to. In this regard we have been\nsuccessful; the principle of the conservation of energy has received\nonly confirmations; a second principle has come to join it, that of\nleast action, put under the form which is suitable for physics. It also\nhas always been verified, at least in so far as concerns reversible\nphenomena which thus obey the equations of Lagrange, that is to say, the\nmost general laws of mechanics.\n\nIrreversible phenomena are much more rebellious. Yet these also are\nbeing coordinated, and tend to come into unity; the light which has\nilluminated them has come to us from Carnot's principle. Long did\nthermodynamics confine itself to the study of the dilatation of bodies\nand their changes of state. For some time past it has been growing\nbolder and has considerably extended its domain. We owe to it the theory\nof the galvanic battery and that of the thermoelectric phenomena; there\nis not in all physics a corner that it has not explored, and it has\nattacked chemistry itself.\n\nEverywhere the same laws reign; everywhere, under the diversity of\nappearances, is found again Carnot's principle; everywhere also is found\nthat concept so prodigiously abstract of entropy, which is as universal\nas that of energy and seems like it to cover a reality. Radiant heat\nseemed destined to escape it; but recently we have seen that submit to\nthe same laws.\n\nIn this way fresh analogies are revealed to us, which may often be\nfollowed into detail; ohmic resistance resembles the viscosity of\nliquids; hysteresis would resemble rather the friction of solids. In all\ncases, friction would appear to be the type which the most various\nirreversible phenomena copy, and this kinship is real and profound.\n\nOf these phenomena a mechanical explanation, properly so called, has\nalso been sought. They hardly lent themselves to it. To find it, it was\nnecessary to suppose that the irreversibility is only apparent, that the\nelementary phenomena are reversible and obey the known laws of dynamics.\nBut the elements are extremely numerous and blend more and more, so that\nto our crude sight all appears to tend toward uniformity, that is,\neverything seems to go forward in the same sense without hope of\nreturn. The apparent irreversibility is thus only an effect of the law\nof great numbers. But, only a being with infinitely subtile senses, like\nMaxwell's imaginary demon, could disentangle this inextricable skein and\nturn back the course of the universe.\n\nThis conception, which attaches itself to the kinetic theory of gases,\nhas cost great efforts and has not, on the whole, been fruitful; but it\nmay become so. This is not the place to examine whether it does not lead\nto contradictions and whether it is in conformity with the true nature\nof things.\n\nWe signalize, however, M. Gouy's original ideas on the Brownian\nmovement. According to this scientist, this singular motion should\nescape Carnot's principle. The particles which it puts in swing would be\nsmaller than the links of that so compacted skein; they would therefore\nbe fitted to disentangle them and hence to make the world go backward.\nWe should almost see Maxwell's demon at work.\n\nTo summarize, the previously known phenomena are better and better\nclassified, but new phenomena come to claim their place; most of these,\nlike the Zeeman effect, have at once found it.\n\nBut we have the cathode rays, the X-rays, those of uranium and of\nradium. Herein is a whole world which no one suspected. How many\nunexpected guests must be stowed away?\n\nNo one can yet foresee the place they will occupy. But I do not believe\nthey will destroy the general unity; I think they will rather complete\nit. On the one hand, in fact, the new radiations seem connected with the\nphenomena of luminescence; not only do they excite fluorescence, but\nthey sometimes take birth in the same conditions as it.\n\nNor are they without kinship with the causes which produce the electric\nspark under the action of the ultra-violet light.\n\nFinally, and above all, it is believed that in all these phenomena are\nfound true ions, animated, it is true, by velocities incomparably\ngreater than in the electrolytes.\n\nThat is all very vague, but it will all become more precise.\n\nPhosphorescence, the action of light on the spark, these were regions\nrather isolated and consequently somewhat neglected by investigators.\nOne may now hope that a new path will be constructed which will\nfacilitate their communications with the rest of science.\n\nNot only do we discover new phenomena, but in those we thought we knew,\nunforeseen aspects reveal themselves. In the free ether, the laws retain\ntheir majestic simplicity; but matter, properly so called, seems more\nand more complex; all that is said of it is never more than approximate,\nand at each instant our formulas require new terms.\n\nNevertheless the frames are not broken; the relations that we have\nrecognized between objects we thought simple still subsist between these\nsame objects when we know their complexity, and it is that alone which\nis of importance. Our equations become, it is true, more and more\ncomplicated, in order to embrace more closely the complexity of nature;\nbut nothing is changed in the relations which permit the deducing of\nthese equations one from another. In a word, the form of these equations\nhas persisted.\n\nTake, for example, the laws of reflection: Fresnel had established them\nby a simple and seductive theory which experiment seemed to confirm.\nSince then more precise researches have proved that this verification\nwas only approximate; they have shown everywhere traces of elliptic\npolarization. But, thanks to the help that the first approximation gave\nus, we found forthwith the cause of these anomalies, which is the\npresence of a transition layer; and Fresnel's theory has subsisted in\nits essentials.\n\nBut there is a reflection we can not help making: All these relations\nwould have remained unperceived if one had at first suspected the\ncomplexity of the objects they connect. It has long been said: If Tycho\nhad had instruments ten times more precise neither Kepler, nor Newton,\nnor astronomy would ever have been. It is a misfortune for a science to\nbe born too late, when the means of observation have become too perfect.\nThis is to-day the case with physical chemistry; its founders are\nembarrassed in their general grasp by third and fourth decimals; happily\nthey are men of a robust faith.\n\nThe better one knows the properties of matter the more one sees\ncontinuity reign. Since the labors of Andrews and of van der Waals, we\nget an idea of how the passage is made from the liquid to the gaseous\nstate and that this passage is not abrupt. Similarly, there is no gap\nbetween the liquid and solid states, and in the proceedings of a recent\ncongress is to be seen, alongside of a work on the rigidity of liquids,\na memoir on the flow of solids.\n\nBy this tendency no doubt simplicity loses; some phenomenon was formerly\nrepresented by several straight lines, now these straights must be\njoined by curves more or less complicated. In compensation unity gains\nnotably. Those cut-off categories quieted the mind, but they did not\nsatisfy it.\n\nFinally the methods of physics have invaded a new domain, that of\nchemistry; physical chemistry is born. It is still very young, but we\nalready see that it will enable us to connect such phenomena as\nelectrolysis, osmosis and the motions of ions.\n\nFrom this rapid exposition, what shall we conclude?\n\nEverything considered, we have approached unity; we have not been as\nquick as was hoped fifty years ago, we have not always taken the\npredicted way; but, finally, we have gained ever so much ground.\n\n\n\n\nCHAPTER XI\n\nTHE CALCULUS OF PROBABILITIES\n\n\nDoubtless it will be astonishing to find here thoughts about the\ncalculus of probabilities. What has it to do with the method of the\nphysical sciences? And yet the questions I shall raise without solving\npresent themselves naturally to the philosopher who is thinking about\nphysics. So far is this the case that in the two preceding chapters I\nhave often been led to use the words 'probability' and 'chance.'\n\n'Predicted facts,' as I have said above, 'can only be probable.'\n\"However solidly founded a prediction may seem to us to be, we are never\nabsolutely sure that experiment will not prove it false. But the\nprobability is often so great that practically we may be satisfied with\nit.\" And a little further on I have added: \"See what a r\u00f4le the belief\nin simplicity plays in our generalizations. We have verified a simple\nlaw in a great number of particular cases; we refuse to admit that this\ncoincidence, so often repeated, can be a mere effect of chance....\"\n\nThus in a multitude of circumstances the physicist is in the same\nposition as the gambler who reckons up his chances. As often as he\nreasons by induction, he requires more or less consciously the calculus\nof probabilities, and this is why I am obliged to introduce a\nparenthesis, and interrupt our study of method in the physical sciences\nin order to examine a little more closely the value of this calculus,\nand what confidence it merits.\n\nThe very name calculus of probabilities is a paradox. Probability\nopposed to certainty is what we do not know, and how can we calculate\nwhat we do not know? Yet many eminent savants have occupied themselves\nwith this calculus, and it can not be denied that science has drawn\ntherefrom no small advantage.\n\nHow can we explain this apparent contradiction?\n\nHas probability been defined? Can it even be defined? And if it can not,\nhow dare we reason about it? The definition, it will be said, is very\nsimple: the probability of an event is the ratio of the number of cases\nfavorable to this event to the total number of possible cases.\n\nA simple example will show how incomplete this definition is. I throw\ntwo dice. What is the probability that one of the two at least turns up\na six? Each die can turn up in six different ways; the number of\npossible cases is 6 \u00d7 6 = 36; the number of favorable cases is 11; the\nprobability is 11/36.\n\nThat is the correct solution. But could I not just as well say: The\npoints which turn up on the two dice can form 6 \u00d7 7/2 = 21 different\ncombinations? Among these combinations 6 are favorable; the probability\nis 6/21.\n\nNow why is the first method of enumerating the possible cases more\nlegitimate than the second? In any case it is not our definition that\ntells us.\n\nWe are therefore obliged to complete this definition by saying: '... to\nthe total number of possible cases provided these cases are equally\nprobable.' So, therefore, we are reduced to defining the probable by the\nprobable.\n\nHow can we know that two possible cases are equally probable? Will it be\nby a convention? If we place at the beginning of each problem an\nexplicit convention, well and good. We shall then have nothing to do but\napply the rules of arithmetic and of algebra, and we shall complete our\ncalculation without our result leaving room for doubt. But if we wish to\nmake the slightest application of this result, we must prove our\nconvention was legitimate, and we shall find ourselves in the presence\nof the very difficulty we thought to escape.\n\nWill it be said that good sense suffices to show us what convention\nshould be adopted? Alas! M. Bertrand has amused himself by discussing\nthe following simple problem: \"What is the probability that a chord of a\ncircle may be greater than the side of the inscribed equilateral\ntriangle?\" The illustrious geometer successively adopted two conventions\nwhich good sense seemed equally to dictate and with one he found 1/2,\nwith the other 1/3.\n\nThe conclusion which seems to follow from all this is that the calculus\nof probabilities is a useless science, and that the obscure instinct\nwhich we may call good sense, and to which we are wont to appeal to\nlegitimatize our conventions, must be distrusted.\n\nBut neither can we subscribe to this conclusion; we can not do without\nthis obscure instinct. Without it science would be impossible, without\nit we could neither discover a law nor apply it. Have we the right, for\ninstance, to enunciate Newton's law? Without doubt, numerous\nobservations are in accord with it; but is not this a simple effect of\nchance? Besides how do we know whether this law, true for so many\ncenturies, will still be true next year? To this objection, you will\nfind nothing to reply, except: 'That is very improbable.'\n\nBut grant the law. Thanks to it, I believe myself able to calculate the\nposition of Jupiter a year from now. Have I the right to believe this?\nWho can tell if a gigantic mass of enormous velocity will not between\nnow and that time pass near the solar system, and produce unforeseen\nperturbations? Here again the only answer is: 'It is very improbable.'\n\nFrom this point of view, all the sciences would be only unconscious\napplications of the calculus of probabilities. To condemn this calculus\nwould be to condemn the whole of science.\n\nI shall dwell lightly on the scientific problems in which the\nintervention of the calculus of probabilities is more evident. In the\nforefront of these is the problem of interpolation, in which, knowing a\ncertain number of values of a function, we seek to divine the\nintermediate values.\n\nI shall likewise mention: the celebrated theory of errors of\nobservation, to which I shall return later; the kinetic theory of gases,\na well-known hypothesis, wherein each gaseous molecule is supposed to\ndescribe an extremely complicated trajectory, but in which, through the\neffect of great numbers, the mean phenomena, alone observable, obey the\nsimple laws of Mariotte and Gay-Lussac.\n\nAll these theories are based on the laws of great numbers, and the\ncalculus of probabilities would evidently involve them in its ruin. It\nis true that they have only a particular interest and that, save as far\nas interpolation is concerned, these are sacrifices to which we might\nreadily be resigned.\n\nBut, as I have said above, it would not be only these partial\nsacrifices that would be in question; it would be the legitimacy of the\nwhole of science that would be challenged.\n\nI quite see that it might be said: \"We are ignorant, and yet we must\nact. For action, we have not time to devote ourselves to an inquiry\nsufficient to dispel our ignorance. Besides, such an inquiry would\ndemand an infinite time. We must therefore decide without knowing; we\nare obliged to do so, hit or miss, and we must follow rules without\nquite believing them. What I know is not that such and such a thing is\ntrue, but that the best course for me is to act as if it were true.\" The\ncalculus of probabilities, and consequently science itself, would\nthenceforth have merely a practical value.\n\nUnfortunately the difficulty does not thus disappear. A gambler wants to\ntry a _coup_; he asks my advice. If I give it to him, I shall use the\ncalculus of probabilities, but I shall not guarantee success. This is\nwhat I shall call _subjective probability_. In this case, we might be\ncontent with the explanation of which I have just given a sketch. But\nsuppose that an observer is present at the game, that he notes all its\n_coups_, and that the game goes on a long time. When he makes a summary\nof his book, he will find that events have taken place in conformity\nwith the laws of the calculus of probabilities. This is what I shall\ncall _objective probability_, and it is this phenomenon which has to be\nexplained.\n\nThere are numerous insurance companies which apply the rules of the\ncalculus of probabilities, and they distribute to their shareholders\ndividends whose objective reality can not be contested. To invoke our\nignorance and the necessity to act does not suffice to explain them.\n\nThus absolute skepticism is not admissible. We may distrust, but we can\nnot condemn _en bloc_. Discussion is necessary.\n\nI. CLASSIFICATION OF THE PROBLEMS OF PROBABILITY.--In order to classify\nthe problems which present themselves _\u00e0 propos_ of probabilities, we\nmay look at them from many different points of view, and, first, from\nthe _point of view of generality_. I have said above that probability is\nthe ratio of the number of favorable cases to the number of possible\ncases. What for want of a better term I call the generality will\nincrease with the number of possible cases. This number may be finite,\nas, for instance, if we take a throw of the dice in which the number of\npossible cases is 36. That is the first degree of generality.\n\nBut if we ask, for example, what is the probability that a point within\na circle is within the inscribed square, there are as many possible\ncases as there are points in the circle, that is to say, an infinity.\nThis is the second degree of generality. Generality can be pushed\nfurther still. We may ask the probability that a function will satisfy a\ngiven condition. There are then as many possible cases as one can\nimagine different functions. This is the third degree of generality, to\nwhich we rise, for instance, when we seek to find the most probable law\nin conformity with a finite number of observations.\n\nWe may place ourselves at a point of view wholly different. If we were\nnot ignorant, there would be no probability, there would be room for\nnothing but certainty. But our ignorance can not be absolute, for then\nthere would no longer be any probability at all, since a little light is\nnecessary to attain even this uncertain science. Thus the problems of\nprobability may be classed according to the greater or less depth of\nthis ignorance.\n\nIn mathematics even we may set ourselves problems of probability. What\nis the probability that the fifth decimal of a logarithm taken at random\nfrom a table is a '9'? There is no hesitation in answering that this\nprobability is 1/10; here we possess all the data of the problem. We can\ncalculate our logarithm without recourse to the table, but we do not\nwish to give ourselves the trouble. This is the first degree of\nignorance.\n\nIn the physical sciences our ignorance becomes greater. The state of a\nsystem at a given instant depends on two things: Its initial state, and\nthe law according to which that state varies. If we know both this law\nand this initial state, we shall have then only a mathematical problem\nto solve, and we fall back upon the first degree of ignorance.\n\nBut it often happens that we know the law, and do not know the initial\nstate. It may be asked, for instance, what is the present distribution\nof the minor planets? We know that from all time they have obeyed the\nlaws of Kepler, but we do not know what was their initial distribution.\n\nIn the kinetic theory of gases, we assume that the gaseous molecules\nfollow rectilinear trajectories, and obey the laws of impact of elastic\nbodies. But, as we know nothing of their initial velocities, we know\nnothing of their present velocities.\n\nThe calculus of probabilities only enables us to predict the mean\nphenomena which will result from the combination of these velocities.\nThis is the second degree of ignorance.\n\nFinally it is possible that not only the initial conditions but the laws\nthemselves are unknown. We then reach the third degree of ignorance and\nin general we can no longer affirm anything at all as to the probability\nof a phenomenon.\n\nIt often happens that instead of trying to guess an event, by means of a\nmore or less imperfect knowledge of the law, the events may be known and\nwe want to find the law; or that instead of deducing effects from\ncauses, we wish to deduce the causes from the effects. These are the\nproblems called _probability of causes_, the most interesting from the\npoint of view of their scientific applications.\n\nI play \u00e9cart\u00e9 with a gentleman I know to be perfectly honest. He is\nabout to deal. What is the probability of his turning up the king? It is\n1/8. This is a problem of the probability of effects.\n\nI play with a gentleman whom I do not know. He has dealt ten times, and\nhe has turned up the king six times. What is the probability that he is\na sharper? This is a problem in the probability of causes.\n\nIt may be said that this is the essential problem of the experimental\nmethod. I have observed _n_ values of _x_ and the corresponding values\nof _y_. I have found that the ratio of the latter to the former is\npractically constant. There is the event, what is the cause?\n\nIs it probable that there is a general law according to which _y_ would\nbe proportional to _x_, and that the small divergencies are due to\nerrors of observation? This is a type of question that one is ever\nasking, and which we unconsciously solve whenever we are engaged in\nscientific work.\n\nI am now going to pass in review these different categories of\nproblems, discussing in succession what I have called above subjective\nand objective probability.\n\nII. PROBABILITY IN MATHEMATICS.--The impossibility of squaring the\ncircle has been proved since 1882; but even before that date all\ngeometers considered that impossibility as so 'probable,' that the\nAcademy of Sciences rejected without examination the alas! too numerous\nmemoirs on this subject, that some unhappy madmen sent in every year.\n\nWas the Academy wrong? Evidently not, and it knew well that in acting\nthus it did not run the least risk of stifling a discovery of moment.\nThe Academy could not have proved that it was right; but it knew quite\nwell that its instinct was not mistaken. If you had asked the\nAcademicians, they would have answered: \"We have compared the\nprobability that an unknown savant should have found out what has been\nvainly sought for so long, with the probability that there is one madman\nthe more on the earth; the second appears to us the greater.\" These are\nvery good reasons, but there is nothing mathematical about them; they\nare purely psychological.\n\nAnd if you had pressed them further they would have added: \"Why do you\nsuppose a particular value of a transcendental function to be an\nalgebraic number; and if [pi] were a root of an algebraic equation, why\ndo you suppose this root to be a period of the function sin 2_x_, and\nnot the same about the other roots of this same equation?\" To sum up,\nthey would have invoked the principle of sufficient reason in its\nvaguest form.\n\nBut what could they deduce from it? At most a rule of conduct for the\nemployment of their time, more usefully spent at their ordinary work\nthan in reading a lucubration that inspired in them a legitimate\ndistrust. But what I call above objective probability has nothing in\ncommon with this first problem.\n\nIt is otherwise with the second problem.\n\nConsider the first 10,000 logarithms that we find in a table. Among\nthese 10,000 logarithms I take one at random. What is the probability\nthat its third decimal is an even number? You will not hesitate to\nanswer 1/2; and in fact if you pick out in a table the third decimals of\nthese 10,000 numbers, you will find nearly as many even digits as odd.\n\nOr if you prefer, let us write 10,000 numbers corresponding to our\n10,000 logarithms, each of these numbers being +1 if the third decimal\nof the corresponding logarithm is even, and -1 if odd. Then take the\nmean of these 10,000 numbers.\n\nI do not hesitate to say that the mean of these 10,000 numbers is\nprobably 0, and if I were actually to calculate it I should verify that\nit is extremely small.\n\nBut even this verification is needless. I might have rigorously proved\nthat this mean is less than 0.003. To prove this result, I should have\nhad to make a rather long calculation for which there is no room here,\nand for which I confine myself to citing an article I published in the\n_Revue g\u00e9n\u00e9rale des Sciences_, April 15, 1899. The only point to which I\nwish to call attention is the following: in this calculation, I should\nhave needed only to rest my case on two facts, to wit, that the first\nand second derivatives of the logarithm remain, in the interval\nconsidered, between certain limits.\n\nHence this important consequence that the property is true not only of\nthe logarithm, but of any continuous function whatever, since the\nderivatives of every continuous function are limited.\n\nIf I was certain beforehand of the result, it is first, because I had\noften observed analogous facts for other continuous functions; and next,\nbecause I made in my mind, in a more or less unconscious and imperfect\nmanner, the reasoning which led me to the preceding inequalities, just\nas a skilled calculator before finishing his multiplication takes into\naccount what it should come to approximately.\n\nAnd besides, since what I call my intuition was only an incomplete\nsummary of a piece of true reasoning, it is clear why observation has\nconfirmed my predictions, and why the objective probability has been in\nagreement with the subjective probability.\n\nAs a third example I shall choose the following problem: A number _u_\nis taken at random, and _n_ is a given very large integer. What is\nthe probable value of sin _nu_? This problem has no meaning by itself.\nTo give it one a convention is needed. We _shall agree_ that the\nprobability for the number _u_ to lie between _a_ and _a_+ is equal to\n[phi](_a_)_da_; that it is therefore proportional to the infinitely\nsmall interval _da_, and equal to this multiplied by _a_ function\n[phi](_a_) depending only on _a_. As for this function, I choose it\narbitrarily, but I must assume it to be continuous. The value of sin\n_nu_ remaining the same when _u_ increases by 2[pi], I may without loss\nof generality assume that _u_ lies between 0 and 2[pi], and I shall thus\nbe led to suppose that [phi](_a_) is a periodic function whose period is\n2[pi].\n\nThe probable value sought is readily expressed by a simple integral, and\nit is easy to show that this integral is less than\n\n 2[pi]M_{_k_}/_n_^{_k_},\n\nM_{_k_} being the maximum value of the _k_th derivative of [phi](_u_).\nWe see then that if the _k_th derivative is finite, our probable value\nwill tend toward 0 when _n_ increases indefinitely, and that more\nrapidly than 1/_n_^{_k_ - 1}.\n\nThe probable value of sin _nu_ when _n_ is very large is therefore\nnaught. To define this value I required a convention; but the result\nremains the same _whatever that convention may be_. I have imposed upon\nmyself only slight restrictions in assuming that the function [phi](_a_)\nis continuous and periodic, and these hypotheses are so natural that we\nmay ask ourselves how they can be escaped.\n\nExamination of the three preceding examples, so different in all\nrespects, has already given us a glimpse, on the one hand, of the r\u00f4le\nof what philosophers call the principle of sufficient reason, and, on\nthe other hand, of the importance of the fact that certain properties\nare common to all continuous functions. The study of probability in the\nphysical sciences will lead us to the same result.\n\nIII. PROBABILITY IN THE PHYSICAL SCIENCES.--We come now to the problems\nconnected with what I have called the second degree of ignorance, those,\nnamely, in which we know the law, but do not know the initial state of\nthe system. I could multiply examples, but will take only one. What is\nthe probable present distribution of the minor planets on the zodiac?\n\nWe know they obey the laws of Kepler. We may even, without at all\nchanging the nature of the problem, suppose that their orbits are all\ncircular, and situated in the same plane, and that we know this plane.\nOn the other hand, we are in absolute ignorance as to what was their\ninitial distribution. However, we do not hesitate to affirm that their\ndistribution is now nearly uniform. Why?\n\nLet _b_ be the longitude of a minor planet in the initial epoch, that is\nto say, the epoch zero. Let _a_ be its mean motion. Its longitude at the\npresent epoch, that is to say at the epoch _t_, will be _at_ + _b_. To\nsay that the present distribution is uniform is to say that the mean\nvalue of the sines and cosines of multiples of _at_ + _b_ is zero. Why\ndo we assert this?\n\nLet us represent each minor planet by a point in a plane, to wit, by a\npoint whose coordinates are precisely _a_ and _b_. All these\nrepresentative points will be contained in a certain region of the\nplane, but as they are very numerous this region will appear dotted with\npoints. We know nothing else about the distribution of these points.\n\nWhat do we do when we wish to apply the calculus of probabilities to\nsuch a question? What is the probability that one or more representative\npoints may be found in a certain portion of the plane? In our ignorance,\nwe are reduced to making an arbitrary hypothesis. To explain the nature\nof this hypothesis, allow me to use, in lieu of a mathematical formula,\na crude but concrete image. Let us suppose that over the surface of our\nplane has been spread an imaginary substance, whose density is variable,\nbut varies continuously. We shall then agree to say that the probable\nnumber of representative points to be found on a portion of the plane is\nproportional to the quantity of fictitious matter found there. If we\nhave then two regions of the plane of the same extent, the probabilities\nthat a representative point of one of our minor planets is found in one\nor the other of these regions will be to one another as the mean\ndensities of the fictitious matter in the one and the other region.\n\nHere then are two distributions, one real, in which the representative\npoints are very numerous, very close together, but discrete like the\nmolecules of matter in the atomic hypothesis; the other remote from\nreality, in which our representative points are replaced by continuous\nfictitious matter. We know that the latter can not be real, but our\nignorance forces us to adopt it.\n\nIf again we had some idea of the real distribution of the representative\npoints, we could arrange it so that in a region of some extent the\ndensity of this imaginary continuous matter would be nearly proportional\nto the number of the representative points, or, if you wish, to the\nnumber of atoms which are contained in that region. Even that is\nimpossible, and our ignorance is so great that we are forced to choose\narbitrarily the function which defines the density of our imaginary\nmatter. Only we shall be forced to a hypothesis from which we can hardly\nget away, we shall suppose that this function is continuous. That is\nsufficient, as we shall see, to enable us to reach a conclusion.\n\nWhat is at the instant _t_ the probable distribution of the minor\nplanets? Or rather what is the probable value of the sine of the\nlongitude at the instant _t_, that is to say of sin (_at_ + _b_)? We\nmade at the outset an arbitrary convention, but if we adopt it, this\nprobable value is entirely defined. Divide the plane into elements of\nsurface. Consider the value of sin (_at_ + _b_) at the center of each of\nthese elements; multiply this value by the surface of the element, and\nby the corresponding density of the imaginary matter. Take then the sum\nfor all the elements of the plane. This sum, by definition, will be the\nprobable mean value we seek, which will thus be expressed by a double\nintegral. It may be thought at first that this mean value depends on the\nchoice of the function which defines the density of the imaginary\nmatter, and that, as this function [phi] is arbitrary, we can, according\nto the arbitrary choice which we make, obtain any mean value. This is\nnot so.\n\nA simple calculation shows that our double integral decreases very\nrapidly when _t_ increases. Thus I could not quite tell what hypothesis\nto make as to the probability of this or that initial distribution; but\nwhatever the hypothesis made, the result will be the same, and this gets\nme out of my difficulty.\n\nWhatever be the function [phi], the mean value tends toward zero as _t_\nincreases, and as the minor planets have certainly accomplished a very\ngreat number of revolutions, I may assert that this mean value is very\nsmall.\n\nI may choose [phi] as I wish, save always one restriction: this function\nmust be continuous; and, in fact, from the point of view of subjective\nprobability, the choice of a discontinuous function would have been\nunreasonable. For instance, what reason could I have for supposing that\nthe initial longitude might be exactly 0\u00b0, but that it could not lie\nbetween 0\u00b0 and 1\u00b0?\n\nBut the difficulty reappears if we take the point of view of objective\nprobability, if we pass from our imaginary distribution in which the\nfictitious matter was supposed continuous to the real distribution in\nwhich our representative points form, as it were, discrete atoms.\n\nThe mean value of sin (_at_ + _b_) will be represented quite simply by\n\n (1/_n_){[Sigma] sin (_at_ + _b_)},\n\n_n_ being the number of minor planets. In lieu of a double integral\nreferring to a continuous function, we shall have a sum of discrete\nterms. And yet no one will seriously doubt that this mean value is\npractically very small.\n\nOur representative points being very close together, our discrete sum\nwill in general differ very little from an integral.\n\nAn integral is the limit toward which a sum of terms tends when the\nnumber of these terms is indefinitely increased. If the terms are very\nnumerous, the sum will differ very little from its limit, that is to say\nfrom the integral, and what I said of this latter will still be true of\nthe sum itself.\n\nNevertheless, there are exceptions. If, for instance, for all the minor\nplanets,\n\n _b_ = [pi]/2 - _at_,\n\nthe longitude for all the planets at the time t would be [pi]/2, and the\nmean value would evidently be equal to unity. For this to be the case,\nit would be necessary that at the epoch 0, the minor planets must have\nall been lying on a spiral of peculiar form, with its spires very close\ntogether. Every one will admit that such an initial distribution is\nextremely improbable (and, even supposing it realized, the distribution\nwould not be uniform at the present time, for example, on January 1,\n1913, but it would become so a few years later).\n\nWhy then do we think this initial distribution improbable? This must be\nexplained, because if we had no reason for rejecting as improbable this\nabsurd hypothesis everything would break down, and we could no longer\nmake any affirmation about the probability of this or that present\ndistribution.\n\nOnce more we shall invoke the principle of sufficient reason to which we\nmust always recur. We might admit that at the beginning the planets were\ndistributed almost in a straight line. We might admit that they were\nirregularly distributed. But it seems to us that there is no sufficient\nreason for the unknown cause that gave them birth to have acted along a\ncurve so regular and yet so complicated, which would appear to have been\nexpressly chosen so that the present distribution would not be uniform.\n\nIV. ROUGE ET NOIR.--The questions raised by games of chance, such as\nroulette, are, fundamentally, entirely analogous to those we have just\ntreated. For example, a wheel is partitioned into a great number of\nequal subdivisions, alternately red and black. A needle is whirled with\nforce, and after having made a great number of revolutions, it stops\nbefore one of these subdivisions. The probability that this division is\nred is evidently 1/2. The needle describes an angle [theta], including\nseveral complete revolutions. I do not know what is the probability that\nthe needle may be whirled with a force such that this angle should lie\nbetween [theta] and [theta]+_d_[theta]; but I can make a convention. I\ncan suppose that this probability is [phi]([theta])_d_[theta]. As for\nthe function [phi]([theta]), I can choose it in an entirely arbitrary\nmanner. There is nothing that can guide me in my choice, but I am\nnaturally led to suppose this function continuous.\n\nLet [epsilon] be the length (measured on the circumference of radius 1)\nof each red and black subdivision. We have to calculate the integral of\n[phi]([theta])_d_[theta], extending it, on the one hand, to all the red\ndivisions and, on the other hand, to all the black divisions, and to\ncompare the results.\n\nConsider an interval 2[epsilon], comprising a red division and a black\ndivision which follows it. Let M and _m_ be the greatest and least\nvalues of the function [phi]([theta]) in this interval. The integral\nextended to the red divisions will be smaller than [Sigma]M[epsilon];\nthe integral extended to the black divisions will be greater than\n[Sigma]_m_[epsilon]; the difference will therefore be less than\n[Sigma](M - _m_)[epsilon]. But, if the function [theta] is supposed\ncontinuous; if, besides, the interval [epsilon] is very small with\nrespect to the total angle described by the needle, the difference\nM - _m_ will be very small. The difference of the two integrals will\ntherefore be very small, and the probability will be very nearly 1/2.\n\nWe see that without knowing anything of the function [theta], I must act\nas if the probability were 1/2. We understand, on the other hand, why,\nif, placing myself at the objective point of view, I observe a certain\nnumber of coups, observation will give me about as many black coups as\nred.\n\nAll players know this objective law; but it leads them into a remarkable\nerror, which has been often exposed, but into which they always fall\nagain. When the red has won, for instance, six times running, they bet\non the black, thinking they are playing a safe game; because, say they,\nit is very rare that red wins seven times running.\n\nIn reality their probability of winning remains 1/2. Observation shows,\nit is true, that series of seven consecutive reds are very rare, but\nseries of six reds followed by a black are just as rare.\n\nThey have noticed the rarity of the series of seven reds; if they have\nnot remarked the rarity of six reds and a black, it is only because such\nseries strike the attention less.\n\nV. THE PROBABILITY OF CAUSES.--We now come to the problems of the\nprobability of causes, the most important from the point of view of\nscientific applications. Two stars, for instance, are very close\ntogether on the celestial sphere. Is this apparent contiguity a mere\neffect of chance? Are these stars, although on almost the same visual\nray, situated at very different distances from the earth, and\nconsequently very far from one another? Or, perhaps, does the apparent\ncorrespond to a real contiguity? This is a problem on the probability of\ncauses.\n\nI recall first that at the outset of all problems of the probability of\neffects that have hitherto occupied us, we have always had to make a\nconvention, more or less justified. And if in most cases the result was,\nin a certain measure, independent of this convention, this was only\nbecause of certain hypotheses which permitted us to reject _a priori_\ndiscontinuous functions, for example, or certain absurd conventions.\n\nWe shall find something analogous when we deal with the probability of\ncauses. An effect may be produced by the cause _A_ or by the cause _B_.\nThe effect has just been observed. We ask the probability that it is due\nto the cause _A_. This is an _a posteriori_ probability of cause. But I\ncould not calculate it, if a convention more or less justified did not\ntell me _in advance_ what is the _a priori_ probability for the cause\n_A_ to come into play; I mean the probability of this event for some one\nwho had not observed the effect.\n\nThe better to explain myself I go back to the example of the game of\n\u00e9cart\u00e9 mentioned above. My adversary deals for the first time and he\nturns up a king. What is the probability that he is a sharper? The\nformulas ordinarily taught give 8/9, a result evidently rather\nsurprising. If we look at it closer, we see that the calculation is made\nas if, _before sitting down at the table_, I had considered that there\nwas one chance in two that my adversary was not honest. An absurd\nhypothesis, because in that case I should have certainly not played with\nhim, and this explains the absurdity of the conclusion.\n\nThe convention about the _a priori_ probability was unjustified, and\nthat is why the calculation of the _a posteriori_ probability led me to\nan inadmissible result. We see the importance of this preliminary\nconvention. I shall even add that if none were made, the problem of the\n_a posteriori_ probability would have no meaning. It must always be made\neither explicitly or tacitly.\n\nPass to an example of a more scientific character. I wish to determine\nan experimental law. This law, when I know it, can be represented by a\ncurve. I make a certain number of isolated observations; each of these\nwill be represented by a point. When I have obtained these different\npoints, I draw a curve between them, striving to pass as near to them as\npossible and yet preserve for my curve a regular form, without angular\npoints, or inflections too accentuated, or brusque variation of the\nradius of curvature. This curve will represent for me the probable law,\nand I assume not only that it will tell me the values of the function\nintermediate between those which have been observed, but also that it\nwill give me the observed values themselves more exactly than direct\nobservation. This is why I make it pass near the points, and not through\nthe points themselves.\n\nHere is a problem in the probability of causes. The effects are the\nmeasurements I have recorded; they depend on a combination of two\ncauses: the true law of the phenomenon and the errors of observation.\nKnowing the effects, we have to seek the probability that the phenomenon\nobeys this law or that, and that the observations have been affected by\nthis or that error. The most probable law then corresponds to the curve\ntraced, and the most probable error of an observation is represented by\nthe distance of the corresponding point from this curve.\n\nBut the problem would have no meaning if, before any observation, I had\nnot fashioned an _a priori_ idea of the probability of this or that law,\nand of the chances of error to which I am exposed.\n\nIf my instruments are good (and that I knew before making the\nobservations), I shall not permit my curve to depart much from the\npoints which represent the rough measurements. If they are bad, I may go\na little further away from them in order to obtain a less sinuous curve;\nI shall sacrifice more to regularity.\n\nWhy then is it that I seek to trace a curve without sinuosities? It is\nbecause I consider _a priori_ a law represented by a continuous function\n(or by a function whose derivatives of high order are small), as more\nprobable than a law not satisfying these conditions. Without this\nbelief, the problem of which we speak would have no meaning;\ninterpolation would be impossible; no law could be deduced from a finite\nnumber of observations; science would not exist.\n\nFifty years ago physicists considered, other things being equal, a\nsimple law as more probable than a complicated law. They even invoked\nthis principle in favor of Mariotte's law as against the experiments of\nRegnault. To-day they have repudiated this belief; and yet, how many\ntimes are they compelled to act as though they still held it! However\nthat may be, what remains of this tendency is the belief in continuity,\nand we have just seen that if this belief were to disappear in its turn,\nexperimental science would become impossible.\n\nVI. THE THEORY OF ERRORS.--We are thus led to speak of the theory of\nerrors, which is directly connected with the problem of the probability\nof causes. Here again we find _effects_, to wit, a certain number of\ndiscordant observations, and we seek to divine the _causes_, which are,\non the one hand, the real value of the quantity to be measured; on the\nother hand, the error made in each isolated observation. It is necessary\nto calculate what is _a posteriori_ the probable magnitude of each\nerror, and consequently the probable value of the quantity to be\nmeasured.\n\nBut as I have just explained, we should not know how to undertake this\ncalculation if we did not admit _a priori_, that is to say, before all\nobservation, a law of probability of errors. Is there a law of errors?\n\nThe law of errors admitted by all calculators is Gauss's law, which is\nrepresented by a certain transcendental curve known under the name of\n'the bell.'\n\nBut first it is proper to recall the classic distinction between\nsystematic and accidental errors. If we measure a length with too long a\nmeter, we shall always find too small a number, and it will be of no use\nto measure several times; this is a systematic error. If we measure with\nan accurate meter, we may, however, make a mistake; but we go wrong, now\ntoo much, now too little, and when we take the mean of a great number of\nmeasurements, the error will tend to grow small. These are accidental\nerrors.\n\nIt is evident from the first that systematic errors can not satisfy\nGauss's law; but do the accidental errors satisfy it? A great number of\ndemonstrations have been attempted; almost all are crude paralogisms.\nNevertheless, we may demonstrate Gauss's law by starting from the\nfollowing hypotheses: the error committed is the result of a great\nnumber of partial and independent errors; each of the partial errors is\nvery little and besides, obeys any law of probability, provided that the\nprobability of a positive error is the same as that of an equal negative\nerror. It is evident that these conditions will be often but not always\nfulfilled, and we may reserve the name of accidental for errors which\nsatisfy them.\n\nWe see that the method of least squares is not legitimate in every case;\nin general the physicists are more distrustful of it than the\nastronomers. This is, no doubt, because the latter, besides the\nsystematic errors to which they and the physicists are subject alike,\nhave to control with an extremely important source of error which is\nwholly accidental; I mean atmospheric undulations. So it is very\ncurious to hear a physicist discuss with an astronomer about a method of\nobservation. The physicist, persuaded that one good measurement is worth\nmore than many bad ones, is before all concerned with eliminating by\ndint of precautions the least systematic errors, and the astronomer says\nto him: 'But thus you can observe only a small number of stars; the\naccidental errors will not disappear.'\n\nWhat should we conclude? Must we continue to use the method of least\nsquares? We must distinguish. We have eliminated all the systematic\nerrors we could suspect; we know well there are still others, but we can\nnot detect them; yet it is necessary to make up our mind and adopt a\ndefinitive value which will be regarded as the probable value; and for\nthat it is evident the best thing to do is to apply Gauss's method. We\nhave only applied a practical rule referring to subjective probability.\nThere is nothing more to be said.\n\nBut we wish to go farther and affirm that not only is the probable value\nso much, but that the probable error in the result is so much. _This is\nabsolutely illegitimate_; it would be true only if we were sure that all\nthe systematic errors were eliminated, and of that we know absolutely\nnothing. We have two series of observations; by applying the rule of\nleast squares, we find that the probable error in the first series is\ntwice as small as in the second. The second series may, however, be\nbetter than the first, because the first perhaps is affected by a large\nsystematic error. All we can say is that the first series is _probably_\nbetter than the second, since its accidental error is smaller, and we\nhave no reason to affirm that the systematic error is greater for one of\nthe series than for the other, our ignorance on this point being\nabsolute.\n\nVII. CONCLUSIONS.--In the lines which precede, I have set many problems\nwithout solving any of them. Yet I do not regret having written them,\nbecause they will perhaps invite the reader to reflect on these delicate\nquestions.\n\nHowever that may be, there are certain points which seem well\nestablished. To undertake any calculation of probability, and even for\nthat calculation to have any meaning, it is necessary to admit, as\npoint of departure, a hypothesis or convention which has always\nsomething arbitrary about it. In the choice of this convention, we can\nbe guided only by the principle of sufficient reason. Unfortunately this\nprinciple is very vague and very elastic, and in the cursory examination\nwe have just made, we have seen it take many different forms. The form\nunder which we have met it most often is the belief in continuity, a\nbelief which it would be difficult to justify by apodeictic reasoning,\nbut without which all science would be impossible. Finally the problems\nto which the calculus of probabilities may be applied with profit are\nthose in which the result is independent of the hypothesis made at the\noutset, provided only that this hypothesis satisfies the condition of\ncontinuity.\n\n\n\n\nCHAPTER XII\n\nOPTICS AND ELECTRICITY\n\n\nFRESNEL'S THEORY.--The best example[5] that can be chosen of physics in\nthe making is the theory of light and its relations to the theory of\nelectricity. Thanks to Fresnel, optics is the best developed part of\nphysics; the so-called wave-theory forms a whole truly satisfying to the\nmind. We must not, however, ask of it what it can not give us.\n\n [5] This chapter is a partial reproduction of the prefaces of two\n of my works: _Th\u00e9orie math\u00e9matique de la lumi\u00e8re_ (Paris, Naud,\n 1889), and _\u00c9lectricit\u00e9 et optique_ (Paris, Naud, 1901).\n\nThe object of mathematical theories is not to reveal to us the true\nnature of things; this would be an unreasonable pretension. Their sole\naim is to coordinate the physical laws which experiment reveals to us,\nbut which, without the help of mathematics, we should not be able even\nto state.\n\nIt matters little whether the ether really exists; that is the affair of\nmetaphysicians. The essential thing for us is that everything happens as\nif it existed, and that this hypothesis is convenient for the\nexplanation of phenomena. After all, have we any other reason to believe\nin the existence of material objects? That, too, is only a convenient\nhypothesis; only this will never cease to be so, whereas, no doubt, some\nday the ether will be thrown aside as useless. But even at that day, the\nlaws of optics and the equations which translate them analytically will\nremain true, at least as a first approximation. It will always be\nuseful, then, to study a doctrine that unites all these equations.\n\nThe undulatory theory rests on a molecular hypothesis. For those who\nthink they have thus discovered the cause under the law, this is an\nadvantage. For the others it is a reason for distrust. But this distrust\nseems to me as little justified as the illusion of the former.\n\nThese hypotheses play only a secondary part. They might be sacrificed.\nThey usually are not, because then the explanation would lose in\nclearness; but that is the only reason.\n\nIn fact, if we looked closer we should see that only two things are\nborrowed from the molecular hypotheses: the principle of the\nconservation of energy and the linear form of the equations, which is\nthe general law of small movements, as of all small variations.\n\nThis explains why most of Fresnel's conclusions remain unchanged when we\nadopt the electromagnetic theory of light.\n\nMAXWELL'S THEORY.--Maxwell, we know, connected by a close bond two parts\nof physics until then entirely foreign to one another, optics and\nelectricity. By blending thus in a vaster whole, in a higher harmony,\nthe optics of Fresnel has not ceased to be alive. Its various parts\nsubsist, and their mutual relations are still the same. Only the\nlanguage we used to express them has changed; and, on the other hand,\nMaxwell has revealed to us other relations, before unsuspected, between\nthe different parts of optics and the domain of electricity.\n\nWhen a French reader first opens Maxwell's book, a feeling of uneasiness\nand often even of mistrust mingles at first with his admiration. Only\nafter a prolonged acquaintance and at the cost of many efforts does this\nfeeling disappear. There are even some eminent minds that never lose it.\n\nWhy are the English scientist's ideas with such difficulty acclimatized\namong us? It is, no doubt, because the education received by the\nmajority of enlightened Frenchmen predisposes them to appreciate\nprecision and logic above every other quality.\n\nThe old theories of mathematical physics gave us in this respect\ncomplete satisfaction. All our masters, from Laplace to Cauchy, have\nproceeded in the same way. Starting from clearly stated hypotheses, they\ndeduced all their consequences with mathematical rigor, and then\ncompared them with experiment. It seemed their aim to give every branch\nof physics the same precision as celestial mechanics.\n\nA mind accustomed to admire such models is hard to suit with a theory.\nNot only will it not tolerate the least appearance of contradiction, but\nit will demand that the various parts be logically connected with one\nanother, and that the number of distinct hypotheses be reduced to\nminimum.\n\nThis is not all; it will have still other demands, which seem to me\nless reasonable. Behind the matter which our senses can reach, and which\nexperiment tells us of, it will desire to see another, and in its eyes\nthe only real, matter, which will have only purely geometric properties,\nand whose atoms will be nothing but mathematical points, subject to the\nlaws of dynamics alone. And yet these atoms, invisible and without\ncolor, it will seek by an unconscious contradiction to represent to\nitself and consequently to identify as closely as possible with common\nmatter.\n\nThen only will it be fully satisfied and imagine that it has penetrated\nthe secret of the universe. If this satisfaction is deceitful, it is\nnone the less difficult to renounce.\n\nThus, on opening Maxwell, a Frenchman expects to find a theoretical\nwhole as logical and precise as the physical optics based on the\nhypothesis of the ether; he thus prepares for himself a disappointment\nwhich I should like to spare the reader by informing him immediately of\nwhat he must look for in Maxwell, and what he can not find there.\n\nMaxwell does not give a mechanical explanation of electricity and\nmagnetism; he confines himself to demonstrating that such an explanation\nis possible.\n\nHe shows also that optical phenomena are only a special case of\nelectromagnetic phenomena. From every theory of electricity, one can\ntherefore deduce immediately a theory of light.\n\nThe converse unfortunately is not true; from a complete explanation of\nlight, it is not always easy to derive a complete explanation of\nelectric phenomena. This is not easy, in particular, if we wish to start\nfrom Fresnel's theory. Doubtless it would not be impossible; but\nnevertheless we must ask whether we are not going to be forced to\nrenounce admirable results that we thought definitely acquired. That\nseems a step backward; and many good minds are not willing to submit to\nit.\n\nWhen the reader shall have consented to limit his hopes, he will still\nencounter other difficulties. The English scientist does not try to\nconstruct a single edifice, final and well ordered; he seems rather to\nerect a great number of provisional and independent constructions,\nbetween which communication is difficult and sometimes impossible.\n\nTake as example the chapter in which he explains electrostatic\nattractions by pressures and tensions in the dielectric medium. This\nchapter might be omitted without making thereby the rest of the book\nless clear or complete; and, on the other hand, it contains a theory\ncomplete in itself which one could understand without having read a\nsingle line that precedes or follows. But it is not only independent of\nthe rest of the work; it is difficult to reconcile with the fundamental\nideas of the book. Maxwell does not even attempt this reconciliation; he\nmerely says: \"I have not been able to make the next step, namely, to\naccount by mechanical considerations for these stresses in the\ndielectric.\"\n\nThis example will suffice to make my thought understood; I could cite\nmany others. Thus who would suspect, in reading the pages devoted to\nmagnetic rotary polarization, that there is an identity between optical\nand magnetic phenomena?\n\nOne must not then flatter himself that he can avoid all contradiction;\nto that it is necessary to be resigned. In fact, two contradictory\ntheories, provided one does not mingle them, and if one does not seek in\nthem the basis of things, may both be useful instruments of research;\nand perhaps the reading of Maxwell would be less suggestive if he had\nnot opened up to us so many new and divergent paths.\n\nThe fundamental idea, however, is thus a little obscured. So far is this\nthe case that in the majority of popularized versions it is the only\npoint completely left aside.\n\nI feel, then, that the better to make its importance stand out, I ought\nto explain in what this fundamental idea consists. But for that a short\ndigression is necessary.\n\nTHE MECHANICAL EXPLANATION OF PHYSICAL PHENOMENA.--There is in every\nphysical phenomenon a certain number of parameters which experiment\nreaches directly and allows us to measure. I shall call these the\nparameters _q_.\n\nObservation then teaches us the laws of the variations of these\nparameters; and these laws can generally be put in the form of\ndifferential equations, which connect the parameters _q_ with the time.\n\nWhat is it necessary to do to give a mechanical interpretation of such a\nphenomenon?\n\nOne will try to explain it either by the motions of ordinary matter, or\nby those of one or more hypothetical fluids.\n\nThese fluids will be considered as formed of a very great number of\nisolated molecules _m_.\n\nWhen shall we say, then, that we have a complete mechanical explanation\nof the phenomenon? It will be, on the one hand, when we know the\ndifferential equations satisfied by the coordinates of these\nhypothetical molecules _m_, equations which, moreover, must conform to\nthe principles of dynamics; and, on the other hand, when we know the\nrelations that define the coordinates of the molecules _m_ as functions\nof the parameters _q_ accessible to experiment.\n\nThese equations, as I have said, must conform to the principles of\ndynamics, and, in particular, to the principle of the conservation of\nenergy and the principle of least action.\n\nThe first of these two principles teaches us that the total energy is\nconstant and that this energy is divided into two parts:\n\n1\u00ba The kinetic energy, or _vis viva_, which depends on the masses of the\nhypothetical molecules _m_, and their velocities, and which I shall call\n_T_.\n\n2\u00ba The potential energy, which depends only on the coordinates of these\nmolecules and which I shall call _U_. It is the _sum_ of the two\nenergies _T_ and _U_ which is constant.\n\nWhat now does the principle of least action tell us? It tells us that to\npass from the initial position occupied at the instant t_{0} to the\nfinal position occupied at the instant t_{1}, the system must take such\na path that, in the interval of time that elapses between the two\ninstants t_{0} and t_{1}, the average value of 'the action' (that is to\nsay, of the _difference_ between the two energies _T_ and _U_) shall be\nas small as possible.\n\nIf the two functions _T_ and _U_ are known, this principle suffices to\ndetermine the equations of motion.\n\nAmong all the possible ways of passing from one position to another,\nthere is evidently one for which the average value of the action is less\nthan for any other. There is, moreover, only one; and it results from\nthis that the principle of least action suffices to determine the path\nfollowed and consequently the equations of motion.\n\nThus we obtain what are called the equations of Lagrange.\n\nIn these equations, the independent variables are the coordinates of the\nhypothetical molecules _m_; but I now suppose that one takes as\nvariables the parameters _q_ directly accessible to experiment.\n\nThe two parts of the energy must then be expressed as functions of the\nparameters _q_ and of their derivatives. They will evidently appear\nunder this form to the experimenter. The latter will naturally try to\ndefine the potential and the kinetic energy by the aid of quantities\nthat he can directly observe.[6]\n\n [6] We add that _U_ will depend only on the parameters _q_, that _T_\n will depend on the parameters _q_ and their derivatives with\n respect to the time and will be a homogeneous polynomial of the\n second degree with respect to these derivatives.\n\nThat granted, the system will always go from one position to another by\na path such that the average action shall be a minimum.\n\nIt matters little that _T_ and _U_ are now expressed by the aid of the\nparameters _q_ and their derivatives; it matters little that it is also\nby means of these parameters that we define the initial and final\npositions; the principle of least action remains always true.\n\nNow here again, of all the paths that lead from one position to another,\nthere is one for which the average action is a minimum, and there is\nonly one. The principle of least action suffices, then, to determine the\ndifferential equations which define the variations of the parameters\n_q_.\n\nThe equations thus obtained are another form of the equations of\nLagrange.\n\nTo form these equations we need to know neither the relations that\nconnect the parameters _q_ with the coordinates of the hypothetical\nmolecules, nor the masses of these molecules, nor the expression of _U_\nas a function of the coordinates of these molecules.\n\nAll we need to know is the expression of _U_ as a function of the\nparameters, and that of _T_ as a function of the parameters _q_ and\ntheir derivatives, that is, the expressions of the kinetic and of the\npotential energy as functions of the experimental data.\n\nThen we shall have one of two things: either for a suitable choice of\nthe functions _T_ and _U_, the equations of Lagrange, constructed as we\nhave just said, will be identical with the differential equations\ndeduced from experiments; or else there will exist no functions _T_ and\n_U_, for which this agreement takes place. In the latter case it is\nclear that no mechanical explanation is possible.\n\nThe _necessary_ condition for a mechanical explanation to be possible is\ntherefore that we can choose the functions _T_ and _U_ in such a way as\nto satisfy the principle of least action, which involves that of the\nconservation of energy.\n\nThis condition, moreover, is _sufficient_. Suppose, in fact, that we\nhave found a function _U_ of the parameters _q_, which represents one of\nthe parts of the energy; that another part of the energy, which we shall\nrepresent by _T_, is a function of the parameters _q_ and their\nderivatives, and that it is a homogeneous polynomial of the second\ndegree with respect to these derivatives; and finally that the equations\nof Lagrange, formed by means of these two functions, _T_ and _U_,\nconform to the data of the experiment.\n\nWhat is necessary in order to deduce from this a mechanical explanation?\nIt is necessary that _U_ can be regarded as the potential energy of a\nsystem and _T_ as the _vis viva_ of the same system.\n\nThere is no difficulty as to _U_, but can _T_ be regarded as the _vis\nviva_ of a material system?\n\nIt is easy to show that this is always possible, and even in an infinity\nof ways. I will confine myself to referring for more details to the\npreface of my work, '\u00c9lectricit\u00e9 et optique.'\n\nThus if the principle of least action can not be satisfied, no\nmechanical explanation is possible; if it can be satisfied, there is not\nonly one, but an infinity, whence it follows that as soon as there is\none there is an infinity of others.\n\nOne more observation.\n\nAmong the quantities that experiment gives us directly, we shall regard\nsome as functions of the coordinates of our hypothetical molecules;\nthese are our parameters _q_. We shall look upon the others as dependent\nnot only on the coordinates, but on the velocities, or, what comes to\nthe same thing, on the derivatives of the parameters _q_, or as\ncombinations of these parameters and their derivatives.\n\nAnd then a question presents itself: among all these quantities measured\nexperimentally, which shall we choose to represent the parameters _q_?\nWhich shall we prefer to regard as the derivatives of these parameters?\nThis choice remains arbitrary to a very large extent; but, for a\nmechanical explanation to be possible, it suffices if we can make the\nchoice in such a way as to accord with the principle of least action.\n\nAnd then Maxwell asked himself whether he could make this choice and\nthat of the two energies _T_ and _U_, in such a way that the electrical\nphenomena would satisfy this principle. Experiment shows us that the\nenergy of an electromagnetic field is decomposed into two parts, the\nelectrostatic energy and the electrodynamic energy. Maxwell observed\nthat if we regard the first as representing the potential energy _U_,\nthe second as representing the kinetic energy _T_; if, moreover, the\nelectrostatic charges of the conductors are considered as parameters _q_\nand the intensities of the currents as the derivatives of other\nparameters _q_; under these conditions, I say, Maxwell observed that the\nelectric phenomena satisfy the principle of least action. Thenceforth he\nwas certain of the possibility of a mechanical explanation.\n\nIf he had explained this idea at the beginning of his book instead of\nrelegating it to an obscure part of the second volume, it would not have\nescaped the majority of readers.\n\nIf, then, a phenomenon admits of a complete mechanical explanation, it\nwill admit of an infinity of others, that will render an account equally\nwell of all the particulars revealed by experiment.\n\nAnd this is confirmed by the history of every branch of physics; in\noptics, for instance, Fresnel believed vibration to be perpendicular to\nthe plane of polarization; Neumann regarded it as parallel to this\nplane. An 'experimentum crucis' has long been sought which would enable\nus to decide between these two theories, but it has not been found.\n\nIn the same way, without leaving the domain of electricity, we may\nascertain that the theory of two fluids and that of the single fluid\nboth account in a fashion equally satisfactory for all the observed laws\nof electrostatics.\n\nAll these facts are easily explicable, thanks to the properties of the\nequations of Lagrange which I have just recalled.\n\nIt is easy now to comprehend what is Maxwell's fundamental idea.\n\nTo demonstrate the possibility of a mechanical explanation of\nelectricity, we need not preoccupy ourselves with finding this\nexplanation itself; it suffices us to know the expression of the two\nfunctions _T_ and _U_, which are the two parts of energy, to form with\nthese two functions the equations of Lagrange and then to compare these\nequations with the experimental laws.\n\nAmong all these possible explanations, how make a choice for which the\naid of experiment fails us? A day will come perhaps when physicists will\nnot interest themselves in these questions, inaccessible to positive\nmethods, and will abandon them to the metaphysicians. This day has not\nyet arrived; man does not resign himself so easily to be forever\nignorant of the foundation of things.\n\nOur choice can therefore be further guided only by considerations where\nthe part of personal appreciation is very great; there are, however,\nsolutions that all the world will reject because of their whimsicality,\nand others that all the world will prefer because of their simplicity.\n\nIn what concerns electricity and magnetism, Maxwell abstains from making\nany choice. It is not that he systematically disdains all that is\nunattainable by positive methods; the time he has devoted to the kinetic\ntheory of gases sufficiently proves that. I will add that if, in his\ngreat work, he develops no complete explanation, he had previously\nattempted to give one in an article in the _Philosophical Magazine_. The\nstrangeness and the complexity of the hypotheses he had been obliged to\nmake had led him afterwards to give this up.\n\nThe same spirit is found throughout the whole work. What is essential,\nthat is to say what must remain common to all theories, is made\nprominent; all that would only be suitable to a particular theory is\nnearly always passed over in silence. Thus the reader finds himself in\nthe presence of a form almost devoid of matter, which he is at first\ntempted to take for a fugitive shadow not to be grasped. But the efforts\nto which he is thus condemned force him to think and he ends by\ncomprehending what was often rather artificial in the theoretic\nconstructs he had previously only wondered at.\n\n\n\n\nCHAPTER XIII\n\nELECTRODYNAMICS\n\n\nThe history of electrodynamics is particularly instructive from our\npoint of view.\n\nAmp\u00e8re entitled his immortal work, 'Th\u00e9orie des ph\u00e9nom\u00e8nes\n\u00e9lectrodynamiques, _uniquement_ fond\u00e9e sur l'exp\u00e9rience.' He therefore\nimagined that he had made _no_ hypothesis, but he had made them, as we\nshall soon see; only he made them without being conscious of it.\n\nHis successors, on the other hand, perceived them, since their attention\nwas attracted by the weak points in Amp\u00e8re's solution. They made new\nhypotheses, of which this time they were fully conscious; but how many\ntimes it was necessary to change them before arriving at the classic\nsystem of to-day which is perhaps not yet final; this we shall see.\n\nI. AMPERE'S THEORY.--When Amp\u00e8re studied experimentally the mutual\nactions of currents, he operated and he only could operate with closed\ncurrents.\n\nIt was not that he denied the possibility of open currents. If two\nconductors are charged with positive and negative electricity and\nbrought into communication by a wire, a current is established going\nfrom one to the other, which continues until the two potentials are\nequal. According to the ideas of Amp\u00e8re's time this was an open current;\nthe current was known to go from the first conductor to the second, it\nwas not seen to return from the second to the first.\n\nSo Amp\u00e8re considered as open currents of this nature, for example, the\ncurrents of discharge of condensers; but he could not make them the\nobjects of his experiments because their duration is too short.\n\nAnother sort of open current may also be imagined. I suppose two\nconductors, _A_ and _B_, connected by a wire _AMB_. Small conducting\nmasses in motion first come in contact with the conductor _B_, take\nfrom it an electric charge, leave contact with _B_ and move along the\npath _BNA_, and, transporting with them their charge, come into contact\nwith _A_ and give to it their charge, which returns then to _B_ along\nthe wire _AMB_.\n\nNow there we have in a sense a closed circuit, since the electricity\ndescribes the closed circuit _BNAMB_; but the two parts of this current\nare very different. In the wire _AMB_, the electricity is displaced\nthrough a fixed conductor, like a voltaic current, overcoming an ohmic\nresistance and developing heat; we say that it is displaced by\nconduction. In the part _BNA_, the electricity is carried by a moving\nconductor; it is said to be displaced by convection.\n\nIf then the current of convection is considered as altogether analogous\nto the current of conduction, the circuit _BNAMB_ is closed; if, on the\ncontrary, the convection current is not 'a true current' and, for\nexample, does not act on the magnet, there remains only the conduction\ncurrent _AMB_, which is open.\n\nFor example, if we connect by a wire the two poles of a Holtz machine,\nthe charged rotating disc transfers the electricity by convection from\none pole to the other, and it returns to the first pole by conduction\nthrough the wire.\n\nBut currents of this sort are very difficult to produce with appreciable\nintensity. With the means at Amp\u00e8re's disposal, we may say that this was\nimpossible.\n\nTo sum up, Amp\u00e8re could conceive of the existence of two kinds of open\ncurrents, but he could operate on neither because they were not strong\nenough or because their duration was too short.\n\nExperiment therefore could only show him the action of a closed current\non a closed current, or, more accurately, the action of a closed current\non a portion of a current, because a current can be made to describe a\nclosed circuit composed of a moving part and a fixed part. It is\npossible then to study the displacements of the moving part under the\naction of another closed current.\n\nOn the other hand, Amp\u00e8re had no means of studying the action of an open\ncurrent, either on a closed current or another open current.\n\n1. _The Case of Closed Currents._--In the case of the mutual action of\ntwo closed currents, experiment revealed to Amp\u00e8re remarkably simple\nlaws.\n\nI recall rapidly here those which will be useful to us in the sequel:\n\n1\u00ba _If the intensity of the currents is kept constant_, and if the two\ncircuits, after having undergone any deformations and displacements\nwhatsoever, return finally to their initial positions, the total work of\nthe electrodynamic actions will be null.\n\nIn other words, there is an _electrodynamic potential_ of the two\ncircuits, proportional to the product of the intensities, and depending\non the form and relative position of the circuits; the work of the\nelectrodynamic actions is equal to the variation of this potential.\n\n2\u00ba The action of a closed solenoid is null.\n\n3\u00ba The action of a circuit _C_ on another voltaic circuit _C'_ depends\nonly on the 'magnetic field' developed by this circuit. At each point in\nspace we can in fact define in magnitude and direction a certain force\ncalled _magnetic force_, which enjoys the following properties:\n\n(_a_) The force exercised by _C_ on a magnetic pole is applied to that\npole and is equal to the magnetic force multiplied by the magnetic mass\nof that pole;\n\n(_b_) A very short magnetic needle tends to take the direction of the\nmagnetic force, and the couple to which it tends to reduce is\nproportional to the magnetic force, the magnetic moment of the needle\nand the sine of the dip of the needle;\n\n(_c_) If the circuit _C_ is displaced, the work of the electrodynamic\naction exercised by _C_ on _C'_ will be equal to the increment of the\n'flow of magnetic force' which passes through the circuit.\n\n2. _Action of a Closed Current on a Portion of Current._--Amp\u00e8re not\nhaving been able to produce an open current, properly so called, had\nonly one way of studying the action of a closed current on a portion of\ncurrent.\n\nThis was by operating on a circuit _C_ composed of two parts, the one\nfixed, the other movable. The movable part was, for instance, a movable\nwire [alpha][beta] whose extremities [alpha] and [beta] could slide\nalong a fixed wire. In one of the positions of the movable wire, the end\n[alpha] rested on the _A_ of the fixed wire and the extremity [beta] on\nthe point _B_ of the fixed wire. The current circulated from [alpha] to\n[beta], that is to say, from _A_ to _B_ along the movable wire, and then\nit returned from _B_ to _A_ along the fixed wire. _This current was\ntherefore closed._\n\nIn a second position, the movable wire having slipped, the extremity\n[alpha] rested on another point _A'_ of the fixed wire, and the\nextremity [beta] on another point _B'_ of the fixed wire. The current\ncirculated then from [alpha] to [beta], that is to say from _A'_ to _B'_\nalong the movable wire, and it afterwards returned from _B'_ to _B_,\nthen from _B_ to _A_, then finally from _A_ to _A'_, always following\nthe fixed wire. The current was therefore also closed.\n\nIf a like current is subjected to the action of a closed current _C_,\nthe movable part will be displaced just as if it were acted upon by a\nforce. Amp\u00e8re _assumes_ that the apparent force to which this movable\npart _AB_ seems thus subjected, representing the action of the _C_ on\nthe portion [alpha][beta] of the current, is the same as if\n[alpha][beta] were traversed by an open current, stopping at [alpha] and\n[beta], in place of being traversed by a closed current which after\narriving at [beta] returns to [alpha] through the fixed part of the\ncircuit.\n\nThis hypothesis seems natural enough, and Amp\u00e8re made it unconsciously;\nnevertheless _it is not necessary_, since we shall see further on that\nHelmholtz rejected it. However that may be, it permitted Amp\u00e8re, though\nhe had never been able to produce an open current, to enunciate the laws\nof the action of a closed current on an open current, or even on an\nelement of current.\n\nThe laws are simple:\n\n1\u00ba The force which acts on an element of current is applied to this\nelement; it is normal to the element and to the magnetic force, and\nproportional to the component of this magnetic force which is normal to\nthe element.\n\n2\u00ba The action of a closed solenoid on an element of current is null.\n\nBut the electrodynamic potential has disappeared, that is to say that,\nwhen a closed current and an open current, whose intensities have been\nmaintained constant, return to their initial positions, the total work\nis not null.\n\n3. _Continuous Rotations._--Among electrodynamic experiments, the most\nremarkable are those in which continuous rotations are produced and\nwhich are sometimes called _unipolar induction_ experiments. A magnet\nmay turn about its axis; a current passes first through a fixed wire,\nenters the magnet by the pole _N_, for example, passes through half the\nmagnet, emerges by a sliding contact and reenters the fixed wire.\n\nThe magnet then begins to rotate continuously without being able ever to\nattain equilibrium; this is Faraday's experiment.\n\nHow is it possible? If it were a question of two circuits of invariable\nform, the one _C_ fixed, the other _C'_ movable about an axis, this\nlatter could never take on continuous rotation; in fact there is an\nelectrodynamic potential; there must therefore be necessarily a position\nof equilibrium when this potential is a maximum.\n\nContinuous rotations are therefore possible only when the circuit _C'_\nis composed of two parts: one fixed, the other movable about an axis, as\nis the case in Faraday's experiment. Here again it is convenient to draw\na distinction. The passage from the fixed to the movable part, or\ninversely, may take place either by simple contact (the same point of\nthe movable part remaining constantly in contact with the same point of\nthe fixed part), or by a sliding contact (the same point of the movable\npart coming successively in contact with diverse points of the fixed\npart).\n\nIt is only in the second case that there can be continuous rotation.\nThis is what then happens: The system tends to take a position of\nequilibrium; but, when at the point of reaching that position, the\nsliding contact puts the movable part in communication with a new point\nof the fixed part; it changes the connections, it changes therefore the\nconditions of equilibrium, so that the position of equilibrium fleeing,\nso to say, before the system which seeks to attain it, rotation may take\nplace indefinitely.\n\nAmp\u00e8re assumes that the action of the circuit on the movable part of\n_C'_ is the same as if the fixed part of _C'_ did not exist, and\ntherefore as if the current passing through the movable part were open.\n\nHe concludes therefore that the action of a closed on an open current,\nor inversely that of an open current on a closed current, may give rise\nto a continuous rotation.\n\nBut this conclusion depends on the hypothesis I have enunciated and\nwhich, as I said above, is not admitted by Helmholtz.\n\n4. _Mutual Action of Two Open Currents._--In what concerns the mutual\nactions of two open currents, and in particular that of two elements of\ncurrent, all experiment breaks down. Amp\u00e8re has recourse to hypothesis.\nHe supposes:\n\n1\u00ba That the mutual action of two elements reduces to a force acting\nalong their join;\n\n2\u00ba That the action of two closed currents is the resultant of the mutual\nactions of their diverse elements, which are besides the same as if\nthese elements were isolated.\n\nWhat is remarkable is that here again Amp\u00e8re makes these hypotheses\nunconsciously.\n\nHowever that may be, these two hypotheses, together with the experiments\non closed currents, suffice to determine completely the law of the\nmutual action of two elements. But then most of the simple laws we have\nmet in the case of closed currents are no longer true.\n\nIn the first place, there is no electrodynamic potential; nor was there\nany, as we have seen, in the case of a closed current acting on an open\ncurrent.\n\nNext there is, properly speaking, no magnetic force.\n\nAnd, in fact, we have given above three different definitions of this\nforce:\n\n1\u00ba By the action on a magnetic pole;\n\n2\u00ba By the director couple which orientates the magnetic needle;\n\n3\u00ba By the action on an element of current.\n\nBut in the case which now occupies us, not only these three definitions\nare no longer in harmony, but each has lost its meaning, and in fact:\n\n1\u00ba A magnetic pole is no longer acted upon simply by a single force\napplied to this pole. We have seen in fact that the force due to the\naction of an element of current on a pole is not applied to the pole,\nbut to the element; it may moreover be replaced by a force applied to\nthe pole and by a couple;\n\n2\u00ba The couple which acts on the magnetic needle is no longer a simple\ndirector couple, for its moment with respect to the axis of the needle\nis not null. It breaks up into a director couple, properly so called,\nand a supplementary couple which tends to produce the continuous\nrotation of which we have above spoken;\n\n3\u00ba Finally the force acting on an element of current is not normal to\nthis element.\n\nIn other words, _the unity of the magnetic force has disappeared_.\n\nLet us see in what this unity consists. Two systems which exercise the\nsame action on a magnetic pole will exert also the same action on an\nindefinitely small magnetic needle, or on an element of current placed\nat the same point of space as this pole.\n\nWell, this is true if these two systems contain only closed currents;\nthis would no longer be true if these two systems contained open\ncurrents.\n\nIt suffices to remark, for instance, that, if a magnetic pole is placed\nat _A_ and an element at _B_, the direction of the element being along\nthe prolongation of the sect _AB_, this element which will exercise no\naction on this pole will, on the other hand, exercise an action either\non a magnetic needle placed at the point _A_, or on an element of\ncurrent placed at the point _A_.\n\n5. _Induction._--We know that the discovery of electrodynamic induction\nsoon followed the immortal work of Amp\u00e8re.\n\nAs long as it is only a question of closed currents there is no\ndifficulty, and Helmholtz has even remarked that the principle of the\nconservation of energy is sufficient for deducing the laws of induction\nfrom the electrodynamic laws of Amp\u00e8re. But always on one condition, as\nBertrand has well shown; that we make besides a certain number of\nhypotheses.\n\nThe same principle again permits this deduction in the case of open\ncurrents, although of course we can not submit the result to the test of\nexperiment, since we can not produce such currents.\n\nIf we try to apply this mode of analysis to Amp\u00e8re's theory of open\ncurrents, we reach results calculated to surprise us.\n\nIn the first place, induction can not be deduced from the variation of\nthe magnetic field by the formula well known to savants and practicians,\nand, in fact, as we have said, properly speaking there is no longer a\nmagnetic field.\n\nBut, further, if a circuit _C_ is subjected to the induction of a\nvariable voltaic system _S_, if this system _S_ be displaced and\ndeformed in any way whatever, so that the intensity of the currents of\nthis system varies according to any law whatever, but that after these\nvariations the system finally returns to its initial situation, it seems\nnatural to suppose that the _mean_ electromotive force induced in the\ncircuit _C_ is null.\n\nThis is true if the circuit _C_ is closed and if the system _S_ contains\nonly closed currents. This would no longer be true, if one accepts the\ntheory of Amp\u00e8re, if there were open currents. So that not only\ninduction will no longer be the variation of the flow of magnetic force,\nin any of the usual senses of the word, but it can not be represented by\nthe variation of anything whatever.\n\nII. THEORY OF HELMHOLTZ.--I have dwelt upon the consequences of Amp\u00e8re's\ntheory, and of his method of explaining open currents.\n\nIt is difficult to overlook the paradoxical and artificial character of\nthe propositions to which we are thus led. One can not help thinking\n'that can not be so.'\n\nWe understand therefore why Helmholtz was led to seek something else.\n\nHelmholtz rejects Amp\u00e8re's fundamental hypothesis, to wit, that the\nmutual action of two elements of current reduces to a force along their\njoin. He assumes that an element of current is not subjected to a single\nforce, but to a force and a couple. It is just this which gave rise to\nthe celebrated polemic between Bertrand and Helmholtz.\n\nHelmholtz replaces Amp\u00e8re's hypothesis by the following: two elements\nalways admit of an electrodynamic potential depending solely on their\nposition and orientation; and the work of the forces that they exercise,\none on the other, is equal to the variation of this potential. Thus\nHelmholtz can no more do without hypothesis than Amp\u00e8re; but at least he\ndoes not make one without explicitly announcing it.\n\nIn the case of closed currents, which are alone accessible to\nexperiment, the two theories agree.\n\nIn all other cases they differ.\n\nIn the first place, contrary to what Amp\u00e8re supposed, the force which\nseems to act on the movable portion of a closed current is not the same\nas would act upon this movable portion if it were isolated and\nconstituted an open current.\n\nLet us return to the circuit _C'_, of which we spoke above, and which\nwas formed of a movable wire [alpha][beta] sliding on a fixed wire. In\nthe only experiment that can be made, the movable portion [alpha][beta]\nis not isolated, but is part of a closed circuit. When it passes from\n_AB_ to _A'B'_, the total electrodynamic potential varies for two\nreasons:\n\n1\u00ba It undergoes a first increase because the potential of _A'B'_ with\nrespect to the circuit _C_ is not the same as that of _AB_;\n\n2\u00ba It takes a second increment because it must be increased by the\npotentials of the elements _AA'_, _BB'_ with respect to _C_.\n\nIt is this _double_ increment which represents the work of the force to\nwhich the portion _AB_ seems subjected.\n\nIf, on the contrary, [alpha][beta] were isolated, the potential would\nundergo only the first increase, and this first increment alone would\nmeasure the work of the force which acts on _AB_.\n\nIn the second place, there could be no continuous rotation without\nsliding contact, and, in fact, that, as we have seen _\u00e0 propos_ of\nclosed currents, is an immediate consequence of the existence of an\nelectrodynamic potential.\n\nIn Faraday's experiment, if the magnet is fixed and if the part of the\ncurrent exterior to the magnet runs along a movable wire, that movable\npart may undergo a continuous rotation. But this does not mean to say\nthat if the contacts of the wire with the magnet were suppressed, and an\n_open_ current were to run along the wire, the wire would still take a\nmovement of continuous rotation.\n\nI have just said in fact that an _isolated_ element is not acted upon in\nthe same way as a movable element making part of a closed circuit.\n\nAnother difference: The action of a closed solenoid on a closed current\nis null according to experiment and according to the two theories. Its\naction on an open current would be null according to Amp\u00e8re; it would\nnot be null according to Helmholtz. From this follows an important\nconsequence. We have given above three definitions of magnetic force.\nThe third has no meaning here since an element of current is no longer\nacted upon by a single force. No more has the first any meaning. What,\nin fact, is a magnetic pole? It is the extremity of an indefinite linear\nmagnet. This magnet may be replaced by an indefinite solenoid. For the\ndefinition of magnetic force to have any meaning, it would be necessary\nthat the action exercised by an open current on an indefinite solenoid\nshould depend only on the position of the extremity of this solenoid,\nthat is to say, that the action on a closed solenoid should be null. Now\nwe have just seen that such is not the case.\n\nOn the other hand, nothing prevents our adopting the second definition,\nwhich is founded on the measurement of the director couple which tends\nto orientate the magnetic needle.\n\nBut if it is adopted, neither the effects of induction nor the\nelectrodynamic effects will depend solely on the distribution of the\nlines of force in this magnetic field.\n\nIII. DIFFICULTIES RAISED BY THESE THEORIES.--The theory of Helmholtz is\nin advance of that of Amp\u00e8re; it is necessary, however, that all the\ndifficulties should be smoothed away. In the one as in the other, the\nphrase 'magnetic field' has no meaning, or, if we give it one, by a more\nor less artificial convention, the ordinary laws so familiar to all\nelectricians no longer apply; thus the electromotive force induced in a\nwire is no longer measured by the number of lines of force met by this\nwire.\n\nAnd our repugnance does not come alone from the difficulty of renouncing\ninveterate habits of language and of thought. There is something more.\nIf we do not believe in action at a distance, electrodynamic phenomena\nmust be explained by a modification of the medium. It is precisely this\nmodification that we call 'magnetic field.' And then the electrodynamic\neffects must depend only on this field.\n\nAll these difficulties arise from the hypothesis of open currents.\n\nIV. MAXWELL'S THEORY.--Such were the difficulties raised by the dominant\ntheories when Maxwell appeared, who with a stroke of the pen made them\nall vanish. To his mind, in fact, all currents are closed currents.\nMaxwell assumes that if in a dielectric the electric field happens to\nvary, this dielectric becomes the seat of a particular phenomenon,\nacting on the galvanometer like a current, and which he calls _current\nof displacement_.\n\nIf then two conductors bearing contrary charges are put in communication\nby a wire, in this wire during the discharge there is an open current of\nconduction; but there are produced at the same time in the surrounding\ndielectric, currents of displacement which close this current of\nconduction.\n\nWe know that Maxwell's theory leads to the explanation of optical\nphenomena, which would be due to extremely rapid electrical\noscillations.\n\nAt that epoch such a conception was only a bold hypothesis, which could\nbe supported by no experiment.\n\nAt the end of twenty years, Maxwell's ideas received the confirmation of\nexperiment. Hertz succeeded in producing systems of electric\noscillations which reproduce all the properties of light, and only\ndiffer from it by the length of their wave; that is to say as violet\ndiffers from red. In some measure he made the synthesis of light.\n\nIt might be said that Hertz has not demonstrated directly Maxwell's\nfundamental idea, the action of the current of displacement on the\ngalvanometer. This is true in a sense. What he has shown in sum is that\nelectromagnetic induction is not propagated instantaneously as was\nsupposed; but with the speed of light.\n\nBut to suppose there is no current of displacement, and induction is\npropagated with the speed of light; or to suppose that the currents of\ndisplacement produce effects of induction, and that the induction is\npropagated instantaneously, _comes to the same thing_.\n\nThis can not be seen at the first glance, but it is proved by an\nanalysis of which I must not think of giving even a summary here.\n\nV. ROWLAND'S EXPERIMENT.--But as I have said above, there are two kinds\nof open conduction currents. There are first the currents of discharge\nof a condenser or of any conductor whatever.\n\nThere are also the cases in which electric discharges describe a closed\ncontour, being displaced by conduction in one part of the circuit and by\nconvection in the other part.\n\nFor open currents of the first sort, the question might be considered as\nsolved; they were closed by the currents of displacement.\n\nFor open currents of the second sort, the solution appeared still more\nsimple. It seemed that if the current were closed, it could only be by\nthe current of convection itself. For that it sufficed to assume that a\n'convection current,' that is to say a charged conductor in motion,\ncould act on the galvanometer.\n\nBut experimental confirmation was lacking. It appeared difficult in fact\nto obtain a sufficient intensity even by augmenting as much as possible\nthe charge and the velocity of the conductors. It was Rowland, an\nextremely skillful experimenter, who first triumphed over these\ndifficulties. A disc received a strong electrostatic charge and a very\ngreat speed of rotation. An astatic magnetic system placed beside the\ndisc underwent deviations.\n\nThe experiment was made twice by Rowland, once in Berlin, once in\nBaltimore. It was afterwards repeated by Himstedt. These physicists even\nannounced that they had succeeded in making quantitative measurements.\n\nIn fact, for twenty years Rowland's law was admitted without objection\nby all physicists. Besides everything seemed to confirm it. The spark\ncertainly does produce a magnetic effect. Now does it not seem probable\nthat the discharge by spark is due to particles taken from one of the\nelectrodes and transferred to the other electrode with their charge? Is\nnot the very spectrum of the spark, in which we recognize the lines of\nthe metal of the electrode, a proof of it? The spark would then be a\nveritable current of convection.\n\nOn the other hand, it is also admitted that in an electrolyte the\nelectricity is carried by the ions in motion. The current in an\nelectrolyte would therefore be also a current of convection; now, it\nacts on the magnetic needle.\n\nThe same for cathode rays. Crookes attributed these rays to a very\nsubtile matter charged with electricity and moving with a very great\nvelocity. He regarded them, in other words, as currents of convection.\nNow these cathode rays are deviated by the magnet. In virtue of the\nprinciple of action and reaction, they should in turn deviate the\nmagnetic needle. It is true that Hertz believed he had demonstrated that\nthe cathode rays do not carry electricity, and that they do not act on\nthe magnetic needle. But Hertz was mistaken. First of all, Perrin\nsucceeded in collecting the electricity carried by these rays,\nelectricity of which Hertz denied the existence; the German scientist\nappears to have been deceived by effects due to the action of X-rays,\nwhich were not yet discovered. Afterwards, and quite recently, the\naction of the cathode rays on the magnetic needle has been put in\nevidence.\n\nThus all these phenomena regarded as currents of convection, sparks,\nelectrolytic currents, cathode rays, act in the same manner on the\ngalvanometer and in conformity with Rowland's law.\n\nVI. THEORY OF LORENTZ.--We soon went farther. According to the theory of\nLorentz, currents of conduction themselves would be true currents of\nconvection. Electricity would remain inseparably connected with certain\nmaterial particles called _electrons_. The circulation of these\nelectrons through bodies would produce voltaic currents. And what would\ndistinguish conductors from insulators would be that the one could be\ntraversed by these electrons while the others would arrest their\nmovements.\n\nThe theory of Lorentz is very attractive. It gives a very simple\nexplanation of certain phenomena which the earlier theories, even\nMaxwell's in its primitive form, could not explain in a satisfactory\nway; for example, the aberration of light, the partial carrying away of\nluminous waves, magnetic polarization and the Zeeman effect.\n\nSome objections still remained. The phenomena of an electric system\nseemed to depend on the absolute velocity of translation of the center\nof gravity of this system, which is contrary to the idea we have of the\nrelativity of space. Supported by M. Cr\u00e9mieu, M. Lippmann has presented\nthis objection in a striking form. Imagine two charged conductors with\nthe same velocity of translation; they are relatively at rest. However,\neach of them being equivalent to a current of convection, they ought to\nattract one another, and by measuring this attraction we could measure\ntheir absolute velocity.\n\n\"No!\" replied the partisans of Lorentz. \"What we could measure in that\nway is not their absolute velocity, but their relative velocity _with\nrespect to the ether_, so that the principle of relativity is safe.\"\n\nWhatever there may be in these latter objections, the edifice of\nelectrodynamics, at least in its broad lines, seemed definitively\nconstructed. Everything was presented under the most satisfactory\naspect. The theories of Amp\u00e8re and of Helmholtz, made for open currents\nwhich no longer existed, seemed to have no longer anything but a purely\nhistoric interest, and the inextricable complications to which these\ntheories led were almost forgotten.\n\nThis quiescence has been recently disturbed by the experiments of M.\nCr\u00e9mieu, which for a moment seemed to contradict the result previously\nobtained by Rowland.\n\nBut fresh researches have not confirmed them, and the theory of Lorentz\nhas victoriously stood the test.\n\nThe history of these variations will be none the less instructive; it\nwill teach us to what pitfalls the scientist is exposed, and how he may\nhope to escape them.\n\n\n * * * * *\n\n\n\n\nTHE VALUE OF SCIENCE\n\n\n\n\n * * * * *\n\n\n\n\nTRANSLATOR'S INTRODUCTION\n\n\n1. _Does the Scientist create Science?_--Professor Rados of Budapest in\nhis report to the Hungarian Academy of Science on the award to Poincar\u00e9\nof the Bolyai prize of ten thousand crowns, speaking of him as\nunquestionably the most powerful investigator in the domain of\nmathematics and mathematical physics, characterized him as the intuitive\ngenius drawing the inspiration for his wide-reaching researches from the\nexhaustless fountain of geometric and physical intuition, yet working\nthis inspiration out in detail with marvelous logical keenness. With his\nbrilliant creative genius was combined the capacity for sharp and\nsuccessful generalization, pushing far out the boundaries of thought in\nthe most widely different domains, so that his works must be ranked with\nthe greatest mathematical achievements of all time. \"Finally,\" says\nRados, \"permit me to make especial mention of his intensely interesting\nbook, 'The Value of Science,' in which he in a way has laid down the\nscientist's creed.\" Now what is this creed?\n\nSense may act as stimulus, as suggestive, yet not to awaken a dormant\ndepiction, or to educe the conception of an archetypal form, but rather\nto strike the hour for creation, to summon to work a sculptor capable of\nsmoothing a Venus of Milo out of the formless clay. Knowledge is not a\ngift of bare experience, nor even made solely out of experience. The\ncreative activity of mind is in mathematics particularly clear. The\naxioms of geometry are conventions, disguised definitions or unprovable\nhypotheses precreated by auto-active animal and human minds. Bertrand\nRussell says of projective geometry: \"It takes nothing from experience,\nand has, like arithmetic, a creature of the pure intellect for its\nobject. It deals with an object whose properties are logically deduced\nfrom its definition, not empirically discovered from data.\" Then does\nthe scientist create science? This is a question Poincar\u00e9 here dissects\nwith a master hand.\n\nThe physiologic-psychologic investigation of the space problem must\ngive the meaning of the words _geometric fact_, _geometric reality_.\nPoincar\u00e9 here subjects to the most successful analysis ever made the\ntridimensionality of our space.\n\n2. _The Mind Dispelling Optical Illusions._--Actual perception of\nspatial properties is accompanied by movements corresponding to its\ncharacter. In the case of optical illusions, with the so-called false\nperceptions eye-movements are closely related. But though the perceived\nobject and its environment remain constant, the sufficiently powerful\nmind can, as we say, dispel these illusions, the perception itself being\ncreatively changed. Photo-graphs taken at intervals during the presence\nof these optical illusions, during the change, perhaps gradual and\nunconscious, in the perception, and after these illusions have, as the\nphrase is, finally disappeared, show quite clearly that changes in\neye-movements corresponding to those internally created in perception\nitself successively occur. What is called accuracy of movement is\ncreated by what is called correctness of perception. The higher creation\nin the perception is the determining cause of an improvement, a\nprecision in the motion. Thus we see correct perception in the\nindividual helping to make that cerebral organization and accurate motor\nadjustment on which its possibility and permanence seem in so far to\ndepend. So-called correct perception is connected with a long-continued\nprocess of perceptual education motived and initiated from within. How\nthis may take place is here illustrated at length by our author.\n\n3. _Euclid not Necessary._--Geometry is a construction of the intellect,\nin application not certain but convenient. As Schiller says, when we see\nthese facts as clearly as the development of metageometry has compelled\nus to see them, we must surely confess that the Kantian account of space\nis hopelessly and demonstrably antiquated. As Royce says in 'Kant's\nDoctrine of the Basis of Mathematics,' \"That very use of intuition which\nKant regarded as geometrically ideal, the modern geometer regards as\nscientifically defective, because surreptitious. No mathematical\nexactness without explicit proof from assumed principles--such is the\nmotto of the modern geometer. But suppose the reasoning of Euclid\npurified of this comparatively surreptitious appeal to intuition.\nSuppose that the principles of geometry are made quite explicit at the\noutset of the treatise, as Pieri and Hilbert or Professor Halsted or Dr.\nVeblen makes his principles explicit in his recent treatment of\ngeometry. Then, indeed, geometry becomes for the modern mathematician a\npurely rational science. But very few students of the logic of\nmathematics at the present time can see any warrant in the analysis of\ngeometrical truth for regarding just the Euclidean system of principles\nas possessing any discoverable necessity.\" Yet the environmental and\nperhaps hereditary premiums on Euclid still make even the scientist\nthink Euclid most convenient.\n\n4. _Without Hypotheses, no Science._--Nobody ever observed an\nequidistantial, but also nobody ever observed a straight line.\nEmerson's Uriel\n\n \"Gave his sentiment divine\n Against the being of a line.\n Line in Nature is not found.\"\n\nClearly not, being an eject from man's mind. What is called 'a knowledge\nof facts' is usually merely a subjective realization that the old\nhypotheses are still sufficiently elastic to serve in some domain; that\nis, with a sufficiency of conscious or unconscious omissions and\ndoctorings and fudgings more or less wilful. In the present book we see\nthe very foundation rocks of science, the conservation of energy and the\nindestructibility of matter, beating against the bars of their cages,\nseemingly anxious to take wing away into the empyrean, to chase the once\ndivine parallel postulate broken loose from Euclid and Kant.\n\n5. _What Outcome?_--What now is the definite, the permanent outcome?\nWhat new islets raise their fronded palms in air within thought's\nmusical domain? Over what age-gray barriers rise the fragrant floods of\nthis new spring-tide, redolent of the wolf-haunted forest of\nTransylvania, of far Erd\u00e9ly's plunging river, Maros the bitter, or broad\nmother Volga at Kazan? What victory heralded the great rocket for which\nyoung Lobachevski, the widow's son, was cast into prison? What severing\nof age-old mental fetters symbolized young Bolyai's cutting-off with\nhis Damascus blade the spikes driven into his door-post, and strewing\nover the sod the thirteen Austrian cavalry officers? This book by the\ngreatest mathematician of our time gives weightiest and most charming\nanswer.\n\n GEORGE BRUCE HALSTED.\n\n\n\n\nINTRODUCTION\n\n\nThe search for truth should be the goal of our activities; it is the\nsole end worthy of them. Doubtless we should first bend our efforts to\nassuage human suffering, but why? Not to suffer is a negative ideal more\nsurely attained by the annihilation of the world. If we wish more and\nmore to free man from material cares, it is that he may be able to\nemploy the liberty obtained in the study and contemplation of truth.\n\nBut sometimes truth frightens us. And in fact we know that it is\nsometimes deceptive, that it is a phantom never showing itself for a\nmoment except to ceaselessly flee, that it must be pursued further and\never further without ever being attained. Yet to work one must stop, as\nsome Greek, Aristotle or another, has said. We also know how cruel the\ntruth often is, and we wonder whether illusion is not more consoling,\nyea, even more bracing, for illusion it is which gives confidence. When\nit shall have vanished, will hope remain and shall we have the courage\nto achieve? Thus would not the horse harnessed to his treadmill refuse\nto go, were his eyes not bandaged? And then to seek truth it is\nnecessary to be independent, wholly independent. If, on the contrary, we\nwish to act, to be strong, we should be united. This is why many of us\nfear truth; we consider it a cause of weakness. Yet truth should not be\nfeared, for it alone is beautiful.\n\nWhen I speak here of truth, assuredly I refer first to scientific truth;\nbut I also mean moral truth, of which what we call justice is only one\naspect. It may seem that I am misusing words, that I combine thus under\nthe same name two things having nothing in common; that scientific\ntruth, which is demonstrated, can in no way be likened to moral truth,\nwhich is felt. And yet I can not separate them, and whosoever loves the\none can not help loving the other. To find the one, as well as to find\nthe other, it is necessary to free the soul completely from prejudice\nand from passion; it is necessary to attain absolute sincerity. These\ntwo sorts of truth when discovered give the same joy; each when\nperceived beams with the same splendor, so that we must see it or close\nour eyes. Lastly, both attract us and flee from us; they are never\nfixed: when we think to have reached them, we find that we have still to\nadvance, and he who pursues them is condemned never to know repose. It\nmust be added that those who fear the one will also fear the other; for\nthey are the ones who in everything are concerned above all with\nconsequences. In a word, I liken the two truths, because the same\nreasons make us love them and because the same reasons make us fear\nthem.\n\nIf we ought not to fear moral truth, still less should we dread\nscientific truth. In the first place it can not conflict with ethics.\nEthics and science have their own domains, which touch but do not\ninterpenetrate. The one shows us to what goal we should aspire, the\nother, given the goal, teaches us how to attain it. So they can never\nconflict since they can never meet. There can no more be immoral science\nthan there can be scientific morals.\n\nBut if science is feared, it is above all because it can not give us\nhappiness. Of course it can not. We may even ask whether the beast does\nnot suffer less than man. But can we regret that earthly paradise where\nman brute-like was really immortal in knowing not that he must die? When\nwe have tasted the apple, no suffering can make us forget its savor. We\nalways come back to it. Could it be otherwise? As well ask if one who\nhas seen and is blind will not long for the light. Man, then, can not be\nhappy through science, but to-day he can much less be happy without it.\n\nBut if truth be the sole aim worth pursuing, may we hope to attain it?\nIt may well be doubted. Readers of my little book 'Science and\nHypothesis' already know what I think about the question. The truth we\nare permitted to glimpse is not altogether what most men call by that\nname. Does this mean that our most legitimate, most imperative\naspiration is at the same time the most vain? Or can we, despite all,\napproach truth on some side? This it is which must be investigated.\n\nIn the first place, what instrument have we at our disposal for this\nconquest? Is not human intelligence, more specifically the intelligence\nof the scientist, susceptible of infinite variation? Volumes could be\nwritten without exhausting this subject; I, in a few brief pages, have\nonly touched it lightly. That the geometer's mind is not like the\nphysicist's or the naturalist's, all the world would agree; but\nmathematicians themselves do not resemble each other; some recognize\nonly implacable logic, others appeal to intuition and see in it the only\nsource of discovery. And this would be a reason for distrust. To minds\nso unlike can the mathematical theorems themselves appear in the same\nlight? Truth which is not the same for all, is it truth? But looking at\nthings more closely, we see how these very different workers collaborate\nin a common task which could not be achieved without their cooperation.\nAnd that already reassures us.\n\nNext must be examined the frames in which nature seems enclosed and\nwhich are called time and space. In 'Science and Hypothesis' I have\nalready shown how relative their value is; it is not nature which\nimposes them upon us, it is we who impose them upon nature because we\nfind them convenient. But I have spoken of scarcely more than space, and\nparticularly quantitative space, so to say, that is of the mathematical\nrelations whose aggregate constitutes geometry. I should have shown that\nit is the same with time as with space and still the same with\n'qualitative space'; in particular, I should have investigated why we\nattribute three dimensions to space. I may be pardoned then for taking\nup again these important questions.\n\nIs mathematical analysis, then, whose principal object is the study of\nthese empty frames, only a vain play of the mind? It can give to the\nphysicist only a convenient language; is this not a mediocre service,\nwhich, strictly speaking, could be done without; and even is it not to\nbe feared that this artificial language may be a veil interposed between\nreality and the eye of the physicist? Far from it; without this language\nmost of the intimate analogies of things would have remained forever\nunknown to us; and we should forever have been ignorant of the internal\nharmony of the world, which is, we shall see, the only true objective\nreality.\n\nThe best expression of this harmony is law. Law is one of the most\nrecent conquests of the human mind; there still are people who live in\nthe presence of a perpetual miracle and are not astonished at it. On the\ncontrary, we it is who should be astonished at nature's regularity. Men\ndemand of their gods to prove their existence by miracles; but the\neternal marvel is that there are not miracles without cease. The world\nis divine because it is a harmony. If it were ruled by caprice, what\ncould prove to us it was not ruled by chance?\n\nThis conquest of law we owe to astronomy, and just this makes the\ngrandeur of the science rather than the material grandeur of the objects\nit considers. It was altogether natural, then, that celestial mechanics\nshould be the first model of mathematical physics; but since then this\nscience has developed; it is still developing, even rapidly developing.\nAnd it is already necessary to modify in certain points the scheme from\nwhich I drew two chapters of 'Science and Hypothesis.' In an address at\nthe St. Louis exposition, I sought to survey the road traveled; the\nresult of this investigation the reader shall see farther on.\n\nThe progress of science has seemed to imperil the best established\nprinciples, those even which were regarded as fundamental. Yet nothing\nshows they will not be saved; and if this comes about only imperfectly,\nthey will still subsist even though they are modified. The advance of\nscience is not comparable to the changes of a city, where old edifices\nare pitilessly torn down to give place to new, but to the continuous\nevolution of zoologic types which develop ceaselessly and end by\nbecoming unrecognizable to the common sight, but where an expert eye\nfinds always traces of the prior work of the centuries past. One must\nnot think then that the old-fashioned theories have been sterile and\nvain.\n\nWere we to stop there, we should find in these pages some reasons for\nconfidence in the value of science, but many more for distrusting it; an\nimpression of doubt would remain; it is needful now to set things to\nrights.\n\nSome people have exaggerated the r\u00f4le of convention in science; they\nhave even gone so far as to say that law, that scientific fact itself,\nwas created by the scientist. This is going much too far in the\ndirection of nominalism. No, scientific laws are not artificial\ncreations; we have no reason to regard them as accidental, though it be\nimpossible to prove they are not.\n\nDoes the harmony the human intelligence thinks it discovers in nature\nexist outside of this intelligence? No, beyond doubt a reality\ncompletely independent of the mind which conceives it, sees or feels it,\nis an impossibility. A world as exterior as that, even if it existed,\nwould for us be forever inaccessible. But what we call objective reality\nis, in the last analysis, what is common to many thinking beings, and\ncould be common to all; this common part, we shall see, can only be the\nharmony expressed by mathematical laws. It is this harmony then which is\nthe sole objective reality, the only truth we can attain; and when I add\nthat the universal harmony of the world is the source of all beauty, it\nwill be understood what price we should attach to the slow and difficult\nprogress which little by little enables us to know it better.\n\n\n\n\nPART I\n\n\nTHE MATHEMATICAL SCIENCES\n\n\n\n\nCHAPTER I\n\nINTUITION AND LOGIC IN MATHEMATICS\n\n\nI\n\nIt is impossible to study the works of the great mathematicians, or even\nthose of the lesser, without noticing and distinguishing two opposite\ntendencies, or rather two entirely different kinds of minds. The one\nsort are above all preoccupied with logic; to read their works, one is\ntempted to believe they have advanced only step by step, after the\nmanner of a Vauban who pushes on his trenches against the place\nbesieged, leaving nothing to chance. The other sort are guided by\nintuition and at the first stroke make quick but sometimes precarious\nconquests, like bold cavalrymen of the advance guard.\n\nThe method is not imposed by the matter treated. Though one often says\nof the first that they are _analysts_ and calls the others _geometers_,\nthat does not prevent the one sort from remaining analysts even when\nthey work at geometry, while the others are still geometers even when\nthey occupy themselves with pure analysis. It is the very nature of\ntheir mind which makes them logicians or intuitionalists, and they can\nnot lay it aside when they approach a new subject.\n\nNor is it education which has developed in them one of the two\ntendencies and stifled the other. The mathematician is born, not made,\nand it seems he is born a geometer or an analyst. I should like to cite\nexamples and there are surely plenty; but to accentuate the contrast I\nshall begin with an extreme example, taking the liberty of seeking it in\ntwo living mathematicians.\n\nM. M\u00e9ray wants to prove that a binomial equation always has a root, or,\nin ordinary words, that an angle may always be subdivided. If there is\nany truth that we think we know by direct intuition, it is this. Who\ncould doubt that an angle may always be divided into any number of equal\nparts? M. M\u00e9ray does not look at it that way; in his eyes this\nproposition is not at all evident and to prove it he needs several\npages.\n\nOn the other hand, look at Professor Klein: he is studying one of the\nmost abstract questions of the theory of functions: to determine whether\non a given Riemann surface there always exists a function admitting of\ngiven singularities. What does the celebrated German geometer do? He\nreplaces his Riemann surface by a metallic surface whose electric\nconductivity varies according to certain laws. He connects two of its\npoints with the two poles of a battery. The current, says he, must pass,\nand the distribution of this current on the surface will define a\nfunction whose singularities will be precisely those called for by the\nenunciation.\n\nDoubtless Professor Klein well knows he has given here only a sketch;\nnevertheless he has not hesitated to publish it; and he would probably\nbelieve he finds in it, if not a rigorous demonstration, at least a kind\nof moral certainty. A logician would have rejected with horror such a\nconception, or rather he would not have had to reject it, because in his\nmind it would never have originated.\n\nAgain, permit me to compare two men, the honor of French science, who\nhave recently been taken from us, but who both entered long ago into\nimmortality. I speak of M. Bertrand and M. Hermite. They were scholars\nof the same school at the same time; they had the same education, were\nunder the same influences; and yet what a difference! Not only does it\nblaze forth in their writings; it is in their teaching, in their way of\nspeaking, in their very look. In the memory of all their pupils these\ntwo faces are stamped in deathless lines; for all who have had the\npleasure of following their teaching, this remembrance is still fresh;\nit is easy for us to evoke it.\n\nWhile speaking, M. Bertrand is always in motion; now he seems in combat\nwith some outside enemy, now he outlines with a gesture of the hand the\nfigures he studies. Plainly he sees and he is eager to paint, this is\nwhy he calls gesture to his aid. With M. Hermite, it is just the\nopposite; his eyes seem to shun contact with the world; it is not\nwithout, it is within he seeks the vision of truth.\n\nAmong the German geometers of this century, two names above all are\nillustrious, those of the two scientists who founded the general theory\nof functions, Weierstrass and Riemann. Weierstrass leads everything back\nto the consideration of series and their analytic transformations; to\nexpress it better, he reduces analysis to a sort of prolongation of\narithmetic; you may turn through all his books without finding a figure.\nRiemann, on the contrary, at once calls geometry to his aid; each of his\nconceptions is an image that no one can forget, once he has caught its\nmeaning.\n\nMore recently, Lie was an intuitionalist; this might have been doubted\nin reading his books, no one could doubt it after talking with him; you\nsaw at once that he thought in pictures. Madame Kovalevski was a\nlogician.\n\nAmong our students we notice the same differences; some prefer to treat\ntheir problems 'by analysis,' others 'by geometry.' The first are\nincapable of 'seeing in space,' the others are quickly tired of long\ncalculations and become perplexed.\n\nThe two sorts of minds are equally necessary for the progress of\nscience; both the logicians and the intuitionalists have achieved great\nthings that others could not have done. Who would venture to say whether\nhe preferred that Weierstrass had never written or that there had never\nbeen a Riemann? Analysis and synthesis have then both their legitimate\nr\u00f4les. But it is interesting to study more closely in the history of\nscience the part which belongs to each.\n\n\nII\n\nStrange! If we read over the works of the ancients we are tempted to\nclass them all among the intuitionalists. And yet nature is always the\nsame; it is hardly probable that it has begun in this century to create\nminds devoted to logic. If we could put ourselves into the flow of ideas\nwhich reigned in their time, we should recognize that many of the old\ngeometers were in tendency analysts. Euclid, for example, erected a\nscientific structure wherein his contemporaries could find no fault. In\nthis vast construction, of which each piece however is due to intuition,\nwe may still to-day, without much effort, recognize the work of a\nlogician.\n\nIt is not minds that have changed, it is ideas; the intuitional minds\nhave remained the same; but their readers have required of them greater\nconcessions.\n\nWhat is the cause of this evolution? It is not hard to find. Intuition\ncan not give us rigor, nor even certainty; this has been recognized more\nand more. Let us cite some examples. We know there exist continuous\nfunctions lacking derivatives. Nothing is more shocking to intuition\nthan this proposition which is imposed upon us by logic. Our fathers\nwould not have failed to say: \"It is evident that every continuous\nfunction has a derivative, since every curve has a tangent.\"\n\nHow can intuition deceive us on this point? It is because when we seek\nto imagine a curve we can not represent it to ourselves without width;\njust so, when we represent to ourselves a straight line, we see it under\nthe form of a rectilinear band of a certain breadth. We well know these\nlines have no width; we try to imagine them narrower and narrower and\nthus to approach the limit; so we do in a certain measure, but we shall\nnever attain this limit. And then it is clear we can always picture\nthese two narrow bands, one straight, one curved, in a position such\nthat they encroach slightly one upon the other without crossing. We\nshall thus be led, unless warned by a rigorous analysis, to conclude\nthat a curve always has a tangent.\n\nI shall take as second example Dirichlet's principle on which rest so\nmany theorems of mathematical physics; to-day we establish it by\nreasoning very rigorous but very long; heretofore, on the contrary, we\nwere content with a very summary proof. A certain integral depending on\nan arbitrary function can never vanish. Hence it is concluded that it\nmust have a minimum. The flaw in this reasoning strikes us immediately,\nsince we use the abstract term _function_ and are familiar with all the\nsingularities functions can present when the word is understood in the\nmost general sense.\n\nBut it would not be the same had we used concrete images, had we, for\nexample, considered this function as an electric potential; it would\nhave been thought legitimate to affirm that electrostatic equilibrium\ncan be attained. Yet perhaps a physical comparison would have awakened\nsome vague distrust. But if care had been taken to translate the\nreasoning into the language of geometry, intermediate between that of\nanalysis and that of physics, doubtless this distrust would not have\nbeen produced, and perhaps one might thus, even to-day, still deceive\nmany readers not forewarned.\n\nIntuition, therefore, does not give us certainty. This is why the\nevolution had to happen; let us now see how it happened.\n\nIt was not slow in being noticed that rigor could not be introduced in\nthe reasoning unless first made to enter into the definitions. For the\nmost part the objects treated of by mathematicians were long ill\ndefined; they were supposed to be known because represented by means of\nthe senses or the imagination; but one had only a crude image of them\nand not a precise idea on which reasoning could take hold. It was there\nfirst that the logicians had to direct their efforts.\n\nSo, in the case of incommensurable numbers. The vague idea of\ncontinuity, which we owe to intuition, resolved itself into a\ncomplicated system of inequalities referring to whole numbers.\n\nBy that means the difficulties arising from passing to the limit, or\nfrom the consideration of infinitesimals, are finally removed. To-day in\nanalysis only whole numbers are left or systems, finite or infinite, of\nwhole numbers bound together by a net of equality or inequality\nrelations. Mathematics, as they say, is arithmetized.\n\n\nIII\n\nA first question presents itself. Is this evolution ended? Have we\nfinally attained absolute rigor? At each stage of the evolution our\nfathers also thought they had reached it. If they deceived themselves,\ndo we not likewise cheat ourselves?\n\nWe believe that in our reasonings we no longer appeal to intuition; the\nphilosophers will tell us this is an illusion. Pure logic could never\nlead us to anything but tautologies; it could create nothing new; not\nfrom it alone can any science issue. In one sense these philosophers are\nright; to make arithmetic, as to make geometry, or to make any science,\nsomething else than pure logic is necessary. To designate this something\nelse we have no word other than _intuition_. But how many different\nideas are hidden under this same word?\n\nCompare these four axioms: (1) Two quantities equal to a third are equal\nto one another; (2) if a theorem is true of the number 1 and if we prove\nthat it is true of _n_ + 1 if true for _n_, then will it be true of all\nwhole numbers; (3) if on a straight the point _C_ is between _A_ and _B_\nand the point _D_ between _A_ and _C_, then the point _D_ will be\nbetween _A_ and _B_; (4) through a given point there is not more than\none parallel to a given straight.\n\nAll four are attributed to intuition, and yet the first is the\nenunciation of one of the rules of formal logic; the second is a real\nsynthetic _a priori_ judgment, it is the foundation of rigorous\nmathematical induction; the third is an appeal to the imagination; the\nfourth is a disguised definition.\n\nIntuition is not necessarily founded on the evidence of the senses; the\nsenses would soon become powerless; for example, we can not represent to\nourselves a chiliagon, and yet we reason by intuition on polygons in\ngeneral, which include the chiliagon as a particular case.\n\nYou know what Poncelet understood by the _principle of continuity_. What\nis true of a real quantity, said Poncelet, should be true of an\nimaginary quantity; what is true of the hyperbola whose asymptotes are\nreal, should then be true of the ellipse whose asymptotes are imaginary.\nPoncelet was one of the most intuitive minds of this century; he was\npassionately, almost ostentatiously, so; he regarded the principle of\ncontinuity as one of his boldest conceptions, and yet this principle did\nnot rest on the evidence of the senses. To assimilate the hyperbola to\nthe ellipse was rather to contradict this evidence. It was only a sort\nof precocious and instinctive generalization which, moreover, I have no\ndesire to defend.\n\nWe have then many kinds of intuition; first, the appeal to the senses\nand the imagination; next, generalization by induction, copied, so to\nspeak, from the procedures of the experimental sciences; finally, we\nhave the intuition of pure number, whence arose the second of the axioms\njust enunciated, which is able to create the real mathematical\nreasoning. I have shown above by examples that the first two can not\ngive us certainty; but who will seriously doubt the third, who will\ndoubt arithmetic?\n\nNow in the analysis of to-day, when one cares to take the trouble to be\nrigorous, there can be nothing but syllogisms or appeals to this\nintuition of pure number, the only intuition which can not deceive us.\nIt may be said that to-day absolute rigor is attained.\n\n\nIV\n\nThe philosophers make still another objection: \"What you gain in rigor,\"\nthey say, \"you lose in objectivity. You can rise toward your logical\nideal only by cutting the bonds which attach you to reality. Your\nscience is infallible, but it can only remain so by imprisoning itself\nin an ivory tower and renouncing all relation with the external world.\nFrom this seclusion it must go out when it would attempt the slightest\napplication.\"\n\nFor example, I seek to show that some property pertains to some object\nwhose concept seems to me at first indefinable, because it is intuitive.\nAt first I fail or must content myself with approximate proofs; finally\nI decide to give to my object a precise definition, and this enables me\nto establish this property in an irreproachable manner.\n\n\"And then,\" say the philosophers, \"it still remains to show that the\nobject which corresponds to this definition is indeed the same made\nknown to you by intuition; or else that some real and concrete object\nwhose conformity with your intuitive idea you believe you immediately\nrecognize corresponds to your new definition. Only then could you affirm\nthat it has the property in question. You have only displaced the\ndifficulty.\"\n\nThat is not exactly so; the difficulty has not been displaced, it has\nbeen divided. The proposition to be established was in reality composed\nof two different truths, at first not distinguished. The first was a\nmathematical truth, and it is now rigorously established. The second was\nan experimental verity. Experience alone can teach us that some real and\nconcrete object corresponds or does not correspond to some abstract\ndefinition. This second verity is not mathematically demonstrated, but\nneither can it be, no more than can the empirical laws of the physical\nand natural sciences. It would be unreasonable to ask more.\n\nWell, is it not a great advance to have distinguished what long was\nwrongly confused? Does this mean that nothing is left of this objection\nof the philosophers? That I do not intend to say; in becoming rigorous,\nmathematical science takes a character so artificial as to strike every\none; it forgets its historical origins; we see how the questions can be\nanswered, we no longer see how and why they are put.\n\nThis shows us that logic is not enough; that the science of\ndemonstration is not all science and that intuition must retain its r\u00f4le\nas complement, I was about to say as counterpoise or as antidote of\nlogic.\n\nI have already had occasion to insist on the place intuition should hold\nin the teaching of the mathematical sciences. Without it young minds\ncould not make a beginning in the understanding of mathematics; they\ncould not learn to love it and would see in it only a vain logomachy;\nabove all, without intuition they would never become capable of applying\nmathematics. But now I wish before all to speak of the r\u00f4le of intuition\nin science itself. If it is useful to the student it is still more so to\nthe creative scientist.\n\n\nV\n\nWe seek reality, but what is reality? The physiologists tell us that\norganisms are formed of cells; the chemists add that cells themselves\nare formed of atoms. Does this mean that these atoms or these cells\nconstitute reality, or rather the sole reality? The way in which these\ncells are arranged and from which results the unity of the individual,\nis not it also a reality much more interesting than that of the isolated\nelements, and should a naturalist who had never studied the elephant\nexcept by means of the microscope think himself sufficiently acquainted\nwith that animal?\n\nWell, there is something analogous to this in mathematics. The logician\ncuts up, so to speak, each demonstration into a very great number of\nelementary operations; when we have examined these operations one after\nthe other and ascertained that each is correct, are we to think we have\ngrasped the real meaning of the demonstration? Shall we have understood\nit even when, by an effort of memory, we have become able to repeat this\nproof by reproducing all these elementary operations in just the order\nin which the inventor had arranged them? Evidently not; we shall not yet\npossess the entire reality; that I know not what, which makes the unity\nof the demonstration, will completely elude us.\n\nPure analysis puts at our disposal a multitude of procedures whose\ninfallibility it guarantees; it opens to us a thousand different ways on\nwhich we can embark in all confidence; we are assured of meeting there\nno obstacles; but of all these ways, which will lead us most promptly to\nour goal? Who shall tell us which to choose? We need a faculty which\nmakes us see the end from afar, and intuition is this faculty. It is\nnecessary to the explorer for choosing his route; it is not less so to\nthe one following his trail who wants to know why he chose it.\n\nIf you are present at a game of chess, it will not suffice, for the\nunderstanding of the game, to know the rules for moving the pieces. That\nwill only enable you to recognize that each move has been made\nconformably to these rules, and this knowledge will truly have very\nlittle value. Yet this is what the reader of a book on mathematics would\ndo if he were a logician only. To understand the game is wholly another\nmatter; it is to know why the player moves this piece rather than that\nother which he could have moved without breaking the rules of the game.\nIt is to perceive the inward reason which makes of this series of\nsuccessive moves a sort of organized whole. This faculty is still more\nnecessary for the player himself, that is, for the inventor.\n\nLet us drop this comparison and return to mathematics. For example, see\nwhat has happened to the idea of continuous function. At the outset this\nwas only a sensible image, for example, that of a continuous mark traced\nby the chalk on a blackboard. Then it became little by little more\nrefined; ere long it was used to construct a complicated system of\ninequalities, which reproduced, so to speak, all the lines of the\noriginal image; this construction finished, the centering of the arch,\nso to say, was removed, that crude representation which had temporarily\nserved as support and which was afterward useless was rejected; there\nremained only the construction itself, irreproachable in the eyes of the\nlogician. And yet if the primitive image had totally disappeared from\nour recollection, how could we divine by what caprice all these\ninequalities were erected in this fashion one upon another?\n\nPerhaps you think I use too many comparisons; yet pardon still another.\nYou have doubtless seen those delicate assemblages of silicious needles\nwhich form the skeleton of certain sponges. When the organic matter has\ndisappeared, there remains only a frail and elegant lace-work. True,\nnothing is there except silica, but what is interesting is the form this\nsilica has taken, and we could not understand it if we did not know the\nliving sponge which has given it precisely this form. Thus it is that\nthe old intuitive notions of our fathers, even when we have abandoned\nthem, still imprint their form upon the logical constructions we have\nput in their place.\n\nThis view of the aggregate is necessary for the inventor; it is equally\nnecessary for whoever wishes really to comprehend the inventor. Can\nlogic give it to us? No; the name mathematicians give it would suffice\nto prove this. In mathematics logic is called _analysis_ and analysis\nmeans _division_, _dissection_. It can have, therefore, no tool other\nthan the scalpel and the microscope.\n\nThus logic and intuition have each their necessary r\u00f4le. Each is\nindispensable. Logic, which alone can give certainty, is the instrument\nof demonstration; intuition is the instrument of invention.\n\n\nVI\n\nBut at the moment of formulating this conclusion I am seized with\nscruples. At the outset I distinguished two kinds of mathematical minds,\nthe one sort logicians and analysts, the others intuitionalists and\ngeometers. Well, the analysts also have been inventors. The names I have\njust cited make my insistence on this unnecessary.\n\nHere is a contradiction, at least apparently, which needs explanation.\nAnd first, do you think these logicians have always proceeded from the\ngeneral to the particular, as the rules of formal logic would seem to\nrequire of them? Not thus could they have extended the boundaries of\nscience; scientific conquest is to be made only by generalization.\n\nIn one of the chapters of 'Science and Hypothesis,' I have had occasion\nto study the nature of mathematical reasoning, and I have shown how this\nreasoning, without ceasing to be absolutely rigorous, could lift us from\nthe particular to the general by a procedure I have called _mathematical\ninduction_. It is by this procedure that the analysts have made science\nprogress, and if we examine the detail itself of their demonstrations,\nwe shall find it there at each instant beside the classic syllogism of\nAristotle. We, therefore, see already that the analysts are not simply\nmakers of syllogisms after the fashion of the scholastics.\n\nBesides, do you think they have always marched step by step with no\nvision of the goal they wished to attain? They must have divined the way\nleading thither, and for that they needed a guide. This guide is, first,\nanalogy. For example, one of the methods of demonstration dear to\nanalysts is that founded on the employment of dominant functions. We\nknow it has already served to solve a multitude of problems; in what\nconsists then the r\u00f4le of the inventor who wishes to apply it to a new\nproblem? At the outset he must recognize the analogy of this question\nwith those which have already been solved by this method; then he must\nperceive in what way this new question differs from the others, and\nthence deduce the modifications necessary to apply to the method.\n\nBut how does one perceive these analogies and these differences? In the\nexample just cited they are almost always evident, but I could have\nfound others where they would have been much more deeply hidden; often a\nvery uncommon penetration is necessary for their discovery. The\nanalysts, not to let these hidden analogies escape them, that is, in\norder to be inventors, must, without the aid of the senses and\nimagination, have a direct sense of what constitutes the unity of a\npiece of reasoning, of what makes, so to speak, its soul and inmost\nlife.\n\nWhen one talked with M. Hermite, he never evoked a sensuous image, and\nyet you soon perceived that the most abstract entities were for him like\nliving beings. He did not see them, but he perceived that they are not\nan artificial assemblage and that they have some principle of internal\nunity.\n\nBut, one will say, that still is intuition. Shall we conclude that the\ndistinction made at the outset was only apparent, that there is only one\nsort of mind and that all the mathematicians are intuitionalists, at\nleast those who are capable of inventing?\n\nNo, our distinction corresponds to something real. I have said above\nthat there are many kinds of intuition. I have said how much the\nintuition of pure number, whence comes rigorous mathematical induction,\ndiffers from sensible intuition to which the imagination, properly so\ncalled, is the principal contributor.\n\nIs the abyss which separates them less profound than it at first\nappeared? Could we recognize with a little attention that this pure\nintuition itself could not do without the aid of the senses? This is the\naffair of the psychologist and the metaphysician and I shall not discuss\nthe question. But the thing's being doubtful is enough to justify me in\nrecognizing and affirming an essential difference between the two kinds\nof intuition; they have not the same object and seem to call into play\ntwo different faculties of our soul; one would think of two\nsearch-lights directed upon two worlds strangers to one another.\n\nIt is the intuition of pure number, that of pure logical forms, which\nillumines and directs those we have called _analysts_. This it is which\nenables them not alone to demonstrate, but also to invent. By it they\nperceive at a glance the general plan of a logical edifice, and that too\nwithout the senses appearing to intervene. In rejecting the aid of the\nimagination, which, as we have seen, is not always infallible, they can\nadvance without fear of deceiving themselves. Happy, therefore, are\nthose who can do without this aid! We must admire them; but how rare\nthey are!\n\nAmong the analysts there will then be inventors, but they will be few.\nThe majority of us, if we wished to see afar by pure intuition alone,\nwould soon feel ourselves seized with vertigo. Our weakness has need of\na staff more solid, and, despite the exceptions of which we have just\nspoken, it is none the less true that sensible intuition is in\nmathematics the most usual instrument of invention.\n\nApropos of these reflections, a question comes up that I have not the\ntime either to solve or even to enunciate with the developments it would\nadmit of. Is there room for a new distinction, for distinguishing among\nthe analysts those who above all use pure intuition and those who are\nfirst of all preoccupied with formal logic?\n\nM. Hermite, for example, whom I have just cited, can not be classed\namong the geometers who make use of the sensible intuition; but neither\nis he a logician, properly so called. He does not conceal his aversion\nto purely deductive procedures which start from the general and end in\nthe particular.\n\n\n\n\nCHAPTER II\n\nTHE MEASURE OF TIME\n\n\nI\n\nSo long as we do not go outside the domain of consciousness, the notion\nof time is relatively clear. Not only do we distinguish without\ndifficulty present sensation from the remembrance of past sensations or\nthe anticipation of future sensations, but we know perfectly well what\nwe mean when we say that of two conscious phenomena which we remember,\none was anterior to the other; or that, of two foreseen conscious\nphenomena, one will be anterior to the other.\n\nWhen we say that two conscious facts are simultaneous, we mean that they\nprofoundly interpenetrate, so that analysis can not separate them\nwithout mutilating them.\n\nThe order in which we arrange conscious phenomena does not admit of any\narbitrariness. It is imposed upon us and of it we can change nothing.\n\nI have only a single observation to add. For an aggregate of sensations\nto have become a remembrance capable of classification in time, it must\nhave ceased to be actual, we must have lost the sense of its infinite\ncomplexity, otherwise it would have remained present. It must, so to\nspeak, have crystallized around a center of associations of ideas which\nwill be a sort of label. It is only when they thus have lost all life\nthat we can classify our memories in time as a botanist arranges dried\nflowers in his herbarium.\n\nBut these labels can only be finite in number. On that score,\npsychologic time should be discontinuous. Whence comes the feeling that\nbetween any two instants there are others? We arrange our recollections\nin time, but we know that there remain empty compartments. How could\nthat be, if time were not a form pre-existent in our minds? How could we\nknow there were empty compartments, if these compartments were revealed\nto us only by their content?\n\n\nII\n\nBut that is not all; into this form we wish to put not only the\nphenomena of our own consciousness, but those of which other\nconsciousnesses are the theater. But more, we wish to put there physical\nfacts, these I know not what with which we people space and which no\nconsciousness sees directly. This is necessary because without it\nscience could not exist. In a word, psychologic time is given to us and\nmust needs create scientific and physical time. There the difficulty\nbegins, or rather the difficulties, for there are two.\n\nThink of two consciousnesses, which are like two worlds impenetrable one\nto the other. By what right do we strive to put them into the same mold,\nto measure them by the same standard? Is it not as if one strove to\nmeasure length with a gram or weight with a meter? And besides, why do\nwe speak of measuring? We know perhaps that some fact is anterior to\nsome other, but not _by how much_ it is anterior.\n\nTherefore two difficulties: (1) Can we transform psychologic time, which\nis qualitative, into a quantitative time? (2) Can we reduce to one and\nthe same measure facts which transpire in different worlds?\n\n\nIII\n\nThe first difficulty has long been noticed; it has been the subject of\nlong discussions and one may say the question is settled. _We have not a\ndirect intuition of the equality of two intervals of time._ The persons\nwho believe they possess this intuition are dupes of an illusion. When I\nsay, from noon to one the same time passes as from two to three, what\nmeaning has this affirmation?\n\nThe least reflection shows that by itself it has none at all. It will\nonly have that which I choose to give it, by a definition which will\ncertainly possess a certain degree of arbitrariness. Psychologists could\nhave done without this definition; physicists and astronomers could not;\nlet us see how they have managed.\n\nTo measure time they use the pendulum and they suppose by definition\nthat all the beats of this pendulum are of equal duration. But this is\nonly a first approximation; the temperature, the resistance of the air,\nthe barometric pressure, make the pace of the pendulum vary. If we\ncould escape these sources of error, we should obtain a much closer\napproximation, but it would still be only an approximation. New causes,\nhitherto neglected, electric, magnetic or others, would introduce minute\nperturbations.\n\nIn fact, the best chronometers must be corrected from time to time, and\nthe corrections are made by the aid of astronomic observations;\narrangements are made so that the sidereal clock marks the same hour\nwhen the same star passes the meridian. In other words, it is the\nsidereal day, that is, the duration of the rotation of the earth, which\nis the constant unit of time. It is supposed, by a new definition\nsubstituted for that based on the beats of the pendulum, that two\ncomplete rotations of the earth about its axis have the same duration.\n\nHowever, the astronomers are still not content with this definition.\nMany of them think that the tides act as a check on our globe, and that\nthe rotation of the earth is becoming slower and slower. Thus would be\nexplained the apparent acceleration of the motion of the moon, which\nwould seem to be going more rapidly than theory permits because our\nwatch, which is the earth, is going slow.\n\n\nIV\n\nAll this is unimportant, one will say; doubtless our instruments of\nmeasurement are imperfect, but it suffices that we can conceive a\nperfect instrument. This ideal can not be reached, but it is enough to\nhave conceived it and so to have put rigor into the definition of the\nunit of time.\n\nThe trouble is that there is no rigor in the definition. When we use the\npendulum to measure time, what postulate do we implicitly admit? _It is\nthat the duration of two identical phenomena is the same_; or, if you\nprefer, that the same causes take the same time to produce the same\neffects.\n\nAnd at first blush, this is a good definition of the equality of two\ndurations. But take care. Is it impossible that experiment may some day\ncontradict our postulate?\n\nLet me explain myself. I suppose that at a certain place in the world\nthe phenomenon [alpha] happens, causing as consequence at the end of a\ncertain time the effect [alpha]'. At another place in the world very\nfar away from the first, happens the phenomenon [beta], which causes as\nconsequence the effect [beta]'. The phenomena [alpha] and [beta] are\nsimultaneous, as are also the effects [alpha]' and [beta]'.\n\nLater, the phenomenon [alpha] is reproduced under approximately the same\nconditions as before, and _simultaneously_ the phenomenon [beta] is also\nreproduced at a very distant place in the world and almost under the\nsame circumstances. The effects [alpha]' and [beta]' also take place.\nLet us suppose that the effect [alpha]' happens perceptibly before the\neffect [beta]'.\n\nIf experience made us witness such a sight, our postulate would be\ncontradicted. For experience would tell us that the first duration\n[alpha][alpha]' is equal to the first duration [beta][beta]' and that\nthe second duration [alpha][alpha]' is less than the second duration\n[beta][beta]'. On the other hand, our postulate would require that the\ntwo durations [alpha][alpha]' should be equal to each other, as likewise\nthe two durations [beta][beta]'. The equality and the inequality deduced\nfrom experience would be incompatible with the two equalities deduced\nfrom the postulate.\n\nNow can we affirm that the hypotheses I have just made are absurd? They\nare in no wise contrary to the principle of contradiction. Doubtless\nthey could not happen without the principle of sufficient reason seeming\nviolated. But to justify a definition so fundamental I should prefer\nsome other guarantee.\n\n\nV\n\nBut that is not all. In physical reality one cause does not produce a\ngiven effect, but a multitude of distinct causes contribute to produce\nit, without our having any means of discriminating the part of each of\nthem.\n\nPhysicists seek to make this distinction; but they make it only\napproximately, and, however they progress, they never will make it\nexcept approximately. It is approximately true that the motion of the\npendulum is due solely to the earth's attraction; but in all rigor every\nattraction, even of Sirius, acts on the pendulum.\n\nUnder these conditions, it is clear that the causes which have produced\na certain effect will never be reproduced except approximately. Then we\nshould modify our postulate and our definition. Instead of saying: 'The\nsame causes take the same time to produce the same effects,' we should\nsay: 'Causes almost identical take almost the same time to produce\nalmost the same effects.'\n\nOur definition therefore is no longer anything but approximate. Besides,\nas M. Calinon very justly remarks in a recent memoir:[7]\n\n One of the circumstances of any phenomenon is the velocity of\n the earth's rotation; if this velocity of rotation varies, it\n constitutes in the reproduction of this phenomenon a\n circumstance which no longer remains the same. But to suppose\n this velocity of rotation constant is to suppose that we know\n how to measure time.\n\n [7] _Etude sur les diverses grandeurs_, Paris, Gauthier-Villars, 1897.\n\nOur definition is therefore not yet satisfactory; it is certainly not\nthat which the astronomers of whom I spoke above implicitly adopt, when\nthey affirm that the terrestrial rotation is slowing down.\n\nWhat meaning according to them has this affirmation? We can only\nunderstand it by analyzing the proofs they give of their proposition.\nThey say first that the friction of the tides producing heat must\ndestroy _vis viva_. They invoke therefore the principle of _vis viva_,\nor of the conservation of energy.\n\nThey say next that the secular acceleration of the moon, calculated\naccording to Newton's law, would be less than that deduced from\nobservations unless the correction relative to the slowing down of the\nterrestrial rotation were made. They invoke therefore Newton's law. In\nother words, they define duration in the following way: time should be\nso defined that Newton's law and that of _vis viva_ may be verified.\nNewton's law is an experimental truth; as such it is only approximate,\nwhich shows that we still have only a definition by approximation.\n\nIf now it be supposed that another way of measuring time is adopted, the\nexperiments on which Newton's law is founded would none the less have\nthe same meaning. Only the enunciation of the law would be different,\nbecause it would be translated into another language; it would evidently\nbe much less simple. So that the definition implicitly adopted by the\nastronomers may be summed up thus: Time should be so defined that the\nequations of mechanics may be as simple as possible. In other words,\nthere is not one way of measuring time more true than another; that\nwhich is generally adopted is only more _convenient_. Of two watches, we\nhave no right to say that the one goes true, the other wrong; we can\nonly say that it is advantageous to conform to the indications of the\nfirst.\n\nThe difficulty which has just occupied us has been, as I have said,\noften pointed out; among the most recent works in which it is\nconsidered, I may mention, besides M. Calinon's little book, the\ntreatise on mechanics of Andrade.\n\n\nVI\n\nThe second difficulty has up to the present attracted much less\nattention; yet it is altogether analogous to the preceding; and even,\nlogically, I should have spoken of it first.\n\nTwo psychological phenomena happen in two different consciousnesses;\nwhen I say they are simultaneous, what do I mean? When I say that a\nphysical phenomenon, which happens outside of every consciousness, is\nbefore or after a psychological phenomenon, what do I mean?\n\nIn 1572, Tycho Brahe noticed in the heavens a new star. An immense\nconflagration had happened in some far distant heavenly body; but it had\nhappened long before; at least two hundred years were necessary for the\nlight from that star to reach our earth. This conflagration therefore\nhappened before the discovery of America. Well, when I say that; when,\nconsidering this gigantic phenomenon, which perhaps had no witness,\nsince the satellites of that star were perhaps uninhabited, I say this\nphenomenon is anterior to the formation of the visual image of the isle\nof Espa\u00f1ola in the consciousness of Christopher Columbus, what do I\nmean?\n\nA little reflection is sufficient to understand that all these\naffirmations have by themselves no meaning. They can have one only as\nthe outcome of a convention.\n\n\nVII\n\nWe should first ask ourselves how one could have had the idea of putting\ninto the same frame so many worlds impenetrable to one another. We\nshould like to represent to ourselves the external universe, and only by\nso doing could we feel that we understood it. We know we never can\nattain this representation: our weakness is too great. But at least we\ndesire the ability to conceive an infinite intelligence for which this\nrepresentation could be possible, a sort of great consciousness which\nshould see all, and which should classify all _in its time_, as we\nclassify, _in our time_, the little we see.\n\nThis hypothesis is indeed crude and incomplete, because this supreme\nintelligence would be only a demigod; infinite in one sense, it would be\nlimited in another, since it would have only an imperfect recollection\nof the past; and it could have no other, since otherwise all\nrecollections would be equally present to it and for it there would be\nno time. And yet when we speak of time, for all which happens outside of\nus, do we not unconsciously adopt this hypothesis; do we not put\nourselves in the place of this imperfect god; and do not even the\natheists put themselves in the place where god would be if he existed?\n\nWhat I have just said shows us, perhaps, why we have tried to put all\nphysical phenomena into the same frame. But that can not pass for a\ndefinition of simultaneity, since this hypothetical intelligence, even\nif it existed, would be for us impenetrable. It is therefore necessary\nto seek something else.\n\n\nVIII\n\nThe ordinary definitions which are proper for psychologic time would\nsuffice us no more. Two simultaneous psychologic facts are so closely\nbound together that analysis can not separate without mutilating them.\nIs it the same with two physical facts? Is not my present nearer my past\nof yesterday than the present of Sirius?\n\nIt has also been said that two facts should be regarded as simultaneous\nwhen the order of their succession may be inverted at will. It is\nevident that this definition would not suit two physical facts which\nhappen far from one another, and that, in what concerns them, we no\nlonger even understand what this reversibility would be; besides,\nsuccession itself must first be defined.\n\n\nIX\n\nLet us then seek to give an account of what is understood by\nsimultaneity or antecedence, and for this let us analyze some examples.\n\nI write a letter; it is afterward read by the friend to whom I have\naddressed it. There are two facts which have had for their theater two\ndifferent consciousnesses. In writing this letter I have had the visual\nimage of it, and my friend has had in his turn this same visual image in\nreading the letter. Though these two facts happen in impenetrable\nworlds, I do not hesitate to regard the first as anterior to the second,\nbecause I believe it is its cause.\n\nI hear thunder, and I conclude there has been an electric discharge; I\ndo not hesitate to consider the physical phenomenon as anterior to the\nauditory image perceived in my consciousness, because I believe it is\nits cause.\n\nBehold then the rule we follow, and the only one we can follow: when a\nphenomenon appears to us as the cause of another, we regard it as\nanterior. It is therefore by cause that we define time; but most often,\nwhen two facts appear to us bound by a constant relation, how do we\nrecognize which is the cause and which the effect? We assume that the\nanterior fact, the antecedent, is the cause of the other, of the\nconsequent. It is then by time that we define cause. How save ourselves\nfrom this _petitio principii_?\n\nWe say now _post hoc, ergo propter hoc_; now _propter hoc, ergo post\nhoc_; shall we escape from this vicious circle?\n\n\nX\n\nLet us see, not how we succeed in escaping, for we do not completely\nsucceed, but how we try to escape.\n\nI execute a voluntary act _A_ and I feel afterward a sensation _D_,\nwhich I regard as a consequence of the act _A_; on the other hand, for\nwhatever reason, I infer that this consequence is not immediate, but\nthat outside my consciousness two facts _B_ and _C_, which I have not\nwitnessed, have happened, and in such a way that _B_ is the effect of\n_A_, that _C_ is the effect of _B_, and _D_ of _C_.\n\nBut why? If I think I have reason to regard the four facts _A_, _B_,\n_C_, _D_, as bound to one another by a causal connection, why range\nthem in the causal order _A B C D_, and at the same time in the\nchronologic order _A B C D_, rather than in any other order?\n\nI clearly see that in the act _A_ I have the feeling of having been\nactive, while in undergoing the sensation _D_ I have that of having been\npassive. This is why I regard _A_ as the initial cause and _D_ as the\nultimate effect; this is why I put _A_ at the beginning of the chain and\n_D_ at the end; but why put _B_ before _C_ rather than _C_ before _B_?\n\nIf this question is put, the reply ordinarily is: we know that it is _B_\nwhich is the cause of _C_ because we always see _B_ happen before _C_.\nThese two phenomena, when witnessed, happen in a certain order; when\nanalogous phenomena happen without witness, there is no reason to invert\nthis order.\n\nDoubtless, but take care; we never know directly the physical phenomena\n_B_ and _C_. What we know are sensations _B'_ and _C'_ produced\nrespectively by _B_ and _C_. Our consciousness tells us immediately that\n_B'_ precedes _C'_ and we suppose that _B_ and _C_ succeed one another\nin the same order.\n\nThis rule appears in fact very natural, and yet we are often led to\ndepart from it. We hear the sound of the thunder only some seconds after\nthe electric discharge of the cloud. Of two flashes of lightning, the\none distant, the other near, can not the first be anterior to the\nsecond, even though the sound of the second comes to us before that of\nthe first?\n\n\nXI\n\nAnother difficulty; have we really the right to speak of the cause of a\nphenomenon? If all the parts of the universe are interchained in a\ncertain measure, any one phenomenon will not be the effect of a single\ncause, but the resultant of causes infinitely numerous; it is, one often\nsays, the consequence of the state of the universe a moment before. How\nenunciate rules applicable to circumstances so complex? And yet it is\nonly thus that these rules can be general and rigorous.\n\nNot to lose ourselves in this infinite complexity, let us make a simpler\nhypothesis. Consider three stars, for example, the sun, Jupiter and\nSaturn; but, for greater simplicity, regard them as reduced to material\npoints and isolated from the rest of the world. The positions and the\nvelocities of three bodies at a given instant suffice to determine their\npositions and velocities at the following instant, and consequently\nat any instant. Their positions at the instant t determine their\npositions at the instant _t_ + _h_ as well as their positions at the\ninstant _t_ - _h_.\n\nEven more; the position of Jupiter at the instant _t_, together with\nthat of Saturn at the instant _t_ + _a_, determines the position of\nJupiter at any instant and that of Saturn at any instant.\n\nThe aggregate of positions occupied by Jupiter at the instant _t_ + _e_\nand Saturn at the instant _t_ + _a_ + _e_ is bound to the aggregate of\npositions occupied by Jupiter at the instant _t_ and Saturn at the\ninstant _t_ + _a_, by laws as precise as that of Newton, though more\ncomplicated. Then why not regard one of these aggregates as the cause of\nthe other, which would lead to considering as simultaneous the instant\n_t_ of Jupiter and the instant _t_ + _a_ of Saturn?\n\nIn answer there can only be reasons, very strong, it is true, of\nconvenience and simplicity.\n\n\nXII\n\nBut let us pass to examples less artificial; to understand the\ndefinition implicitly supposed by the savants, let us watch them at work\nand look for the rules by which they investigate simultaneity.\n\nI will take two simple examples, the measurement of the velocity of\nlight and the determination of longitude.\n\nWhen an astronomer tells me that some stellar phenomenon, which his\ntelescope reveals to him at this moment, happened, nevertheless, fifty\nyears ago, I seek his meaning, and to that end I shall ask him first how\nhe knows it, that is, how he has measured the velocity of light.\n\nHe has begun by _supposing_ that light has a constant velocity, and in\nparticular that its velocity is the same in all directions. That is a\npostulate without which no measurement of this velocity could be\nattempted. This postulate could never be verified directly by\nexperiment; it might be contradicted by it if the results of different\nmeasurements were not concordant. We should think ourselves fortunate\nthat this contradiction has not happened and that the slight\ndiscordances which may happen can be readily explained.\n\nThe postulate, at all events, resembling the principle of sufficient\nreason, has been accepted by everybody; what I wish to emphasize is that\nit furnishes us with a new rule for the investigation of simultaneity,\nentirely different from that which we have enunciated above.\n\nThis postulate assumed, let us see how the velocity of light has been\nmeasured. You know that Roemer used eclipses of the satellites of\nJupiter, and sought how much the event fell behind its prediction. But\nhow is this prediction made? It is by the aid of astronomic laws; for\ninstance Newton's law.\n\nCould not the observed facts be just as well explained if we attributed\nto the velocity of light a little different value from that adopted, and\nsupposed Newton's law only approximate? Only this would lead to\nreplacing Newton's law by another more complicated. So for the velocity\nof light a value is adopted, such that the astronomic laws compatible\nwith this value may be as simple as possible. When navigators or\ngeographers determine a longitude, they have to solve just the problem\nwe are discussing; they must, without being at Paris, calculate Paris\ntime. How do they accomplish it? They carry a chronometer set for Paris.\nThe qualitative problem of simultaneity is made to depend upon the\nquantitative problem of the measurement of time. I need not take up the\ndifficulties relative to this latter problem, since above I have\nemphasized them at length.\n\nOr else they observe an astronomic phenomenon, such as an eclipse of the\nmoon, and they suppose that this phenomenon is perceived simultaneously\nfrom all points of the earth. That is not altogether true, since the\npropagation of light is not instantaneous; if absolute exactitude were\ndesired, there would be a correction to make according to a complicated\nrule.\n\nOr else finally they use the telegraph. It is clear first that the\nreception of the signal at Berlin, for instance, is after the sending of\nthis same signal from Paris. This is the rule of cause and effect\nanalyzed above. But how much after? In general, the duration of the\ntransmission is neglected and the two events are regarded as\nsimultaneous. But, to be rigorous, a little correction would still have\nto be made by a complicated calculation; in practise it is not made,\nbecause it would be well within the errors of observation; its theoretic\nnecessity is none the less from our point of view, which is that of a\nrigorous definition. From this discussion, I wish to emphasize two\nthings: (1) The rules applied are exceedingly various. (2) It is\ndifficult to separate the qualitative problem of simultaneity from the\nquantitative problem of the measurement of time; no matter whether a\nchronometer is used, or whether account must be taken of a velocity of\ntransmission, as that of light, because such a velocity could not be\nmeasured without _measuring_ a time.\n\n\nXIII\n\nTo conclude: We have not a direct intuition of simultaneity, nor of the\nequality of two durations. If we think we have this intuition, this is\nan illusion. We replace it by the aid of certain rules which we apply\nalmost always without taking count of them.\n\nBut what is the nature of these rules? No general rule, no rigorous\nrule; a multitude of little rules applicable to each particular case.\n\nThese rules are not imposed upon us and we might amuse ourselves in\ninventing others; but they could not be cast aside without greatly\ncomplicating the enunciation of the laws of physics, mechanics and\nastronomy.\n\nWe therefore choose these rules, not because they are true, but because\nthey are the most convenient, and we may recapitulate them as follows:\n\"The simultaneity of two events, or the order of their succession, the\nequality of two durations, are to be so defined that the enunciation of\nthe natural laws may be as simple as possible. In other words, all these\nrules, all these definitions are only the fruit of an unconscious\nopportunism.\"\n\n\n\n\nCHAPTER III\n\nTHE NOTION OF SPACE\n\n\n1. _Introduction_\n\nIn the articles I have heretofore devoted to space I have above all\nemphasized the problems raised by non-Euclidean geometry, while leaving\nalmost completely aside other questions more difficult of approach, such\nas those which pertain to the number of dimensions. All the geometries I\nconsidered had thus a common basis, that tridimensional continuum which\nwas the same for all and which differentiated itself only by the figures\none drew in it or when one aspired to measure it.\n\nIn this continuum, primitively amorphous, we may imagine a network of\nlines and surfaces, we may then convene to regard the meshes of this net\nas equal to one another, and it is only after this convention that this\ncontinuum, become measurable, becomes Euclidean or non-Euclidean space.\nFrom this amorphous continuum can therefore arise indifferently one or\nthe other of the two spaces, just as on a blank sheet of paper may be\ntraced indifferently a straight or a circle.\n\nIn space we know rectilinear triangles the sum of whose angles is equal\nto two right angles; but equally we know curvilinear triangles the sum\nof whose angles is less than two right angles. The existence of the one\nsort is not more doubtful than that of the other. To give the name of\nstraights to the sides of the first is to adopt Euclidean geometry; to\ngive the name of straights to the sides of the latter is to adopt the\nnon-Euclidean geometry. So that to ask what geometry it is proper to\nadopt is to ask, to what line is it proper to give the name straight?\n\nIt is evident that experiment can not settle such a question; one would\nnot ask, for instance, experiment to decide whether I should call _AB_\nor _CD_ a straight. On the other hand, neither can I say that I have not\nthe right to give the name of straights to the sides of non-Euclidean\ntriangles because they are not in conformity with the eternal idea of\nstraight which I have by intuition. I grant, indeed, that I have the\nintuitive idea of the side of the Euclidean triangle, but I have equally\nthe intuitive idea of the side of the non-Euclidean triangle. Why should\nI have the right to apply the name of straight to the first of these\nideas and not to the second? Wherein does this syllable form an\nintegrant part of this intuitive idea? Evidently when we say that the\nEuclidean straight is a _true_ straight and that the non-Euclidean\nstraight is not a true straight, we simply mean that the first intuitive\nidea corresponds to a _more noteworthy_ object than the second. But how\ndo we decide that this object is more noteworthy? This question I have\ninvestigated in 'Science and Hypothesis.'\n\nIt is here that we saw experience come in. If the Euclidean straight is\nmore noteworthy than the non-Euclidean straight, it is so chiefly\nbecause it differs little from certain noteworthy natural objects from\nwhich the non-Euclidean straight differs greatly. But, it will be said,\nthe definition of the non-Euclidean straight is artificial; if we for a\nmoment adopt it, we shall see that two circles of different radius both\nreceive the name of non-Euclidean straights, while of two circles of the\nsame radius one can satisfy the definition without the other being able\nto satisfy it, and then if we transport one of these so-called straights\nwithout deforming it, it will cease to be a straight. But by what right\ndo we consider as equal these two figures which the Euclidean geometers\ncall two circles with the same radius? It is because by transporting one\nof them without deforming it we can make it coincide with the other. And\nwhy do we say this transportation is effected without deformation? It is\nimpossible to give a good reason for it. Among all the motions\nconceivable, there are some of which the Euclidean geometers say that\nthey are not accompanied by deformation; but there are others of which\nthe non-Euclidean geometers would say that they are not accompanied by\ndeformation. In the first, called Euclidean motions, the Euclidean\nstraights remain Euclidean straights and the non-Euclidean straights do\nnot remain non-Euclidean straights; in the motions of the second sort,\nor non-Euclidean motions, the non-Euclidean straights remain\nnon-Euclidean straights and the Euclidean straights do not remain\nEuclidean straights. It has, therefore, not been demonstrated that it\nwas unreasonable to call straights the sides of non-Euclidean triangles;\nit has only been shown that that would be unreasonable if one continued\nto call the Euclidean motions motions without deformation; but it has at\nthe same time been shown that it would be just as unreasonable to call\nstraights the sides of Euclidean triangles if the non-Euclidean motions\nwere called motions without deformation.\n\nNow when we say that the Euclidean motions are the _true_ motions\nwithout deformation, what do we mean? We simply mean that they are _more\nnoteworthy_ than the others. And why are they more noteworthy? It is\nbecause certain noteworthy natural bodies, the solid bodies, undergo\nmotions almost similar.\n\nAnd then when we ask: Can one imagine non-Euclidean space? That means:\nCan we imagine a world where there would be noteworthy natural objects\naffecting almost the form of non-Euclidean straights, and noteworthy\nnatural bodies frequently undergoing motions almost similar to the\nnon-Euclidean motions? I have shown in 'Science and Hypothesis' that to\nthis question we must answer yes.\n\nIt has often been observed that if all the bodies in the universe were\ndilated simultaneously and in the same proportion, we should have no\nmeans of perceiving it, since all our measuring instruments would grow\nat the same time as the objects themselves which they serve to measure.\nThe world, after this dilatation, would continue on its course without\nanything apprising us of so considerable an event. In other words, two\nworlds similar to one another (understanding the word similitude in the\nsense of Euclid, Book VI.) would be absolutely indistinguishable. But\nmore; worlds will be indistinguishable not only if they are equal or\nsimilar, that is, if we can pass from one to the other by changing the\naxes of coordinates, or by changing the scale to which lengths are\nreferred; but they will still be indistinguishable if we can pass from\none to the other by any 'point-transformation' whatever. I will explain\nmy meaning. I suppose that to each point of one corresponds one point of\nthe other and only one, and inversely; and besides that the coordinates\nof a point are continuous functions, _otherwise altogether arbitrary_,\nof the corresponding point. I suppose besides that to each object of the\nfirst world corresponds in the second an object of the same nature\nplaced precisely at the corresponding point. I suppose finally that this\ncorrespondence fulfilled at the initial instant is maintained\nindefinitely. We should have no means of distinguishing these two worlds\none from the other. The relativity of space is not ordinarily understood\nin so broad a sense; it is thus, however, that it would be proper to\nunderstand it.\n\nIf one of these universes is our Euclidean world, what its inhabitants\nwill call straight will be our Euclidean straight; but what the\ninhabitants of the second world will call straight will be a curve which\nwill have the same properties in relation to the world they inhabit and\nin relation to the motions that they will call motions without\ndeformation. Their geometry will, therefore, be Euclidean geometry, but\ntheir straight will not be our Euclidean straight. It will be its\ntransform by the point-transformation which carries over from our world\nto theirs. The straights of these men will not be our straights, but\nthey will have among themselves the same relations as our straights to\none another. It is in this sense I say their geometry will be ours. If\nthen we wish after all to proclaim that they deceive themselves, that\ntheir straight is not the true straight, if we still are unwilling to\nadmit that such an affirmation has no meaning, at least we must confess\nthat these people have no means whatever of recognizing their error.\n\n\n2. _Qualitative Geometry_\n\nAll that is relatively easy to understand, and I have already so often\nrepeated it that I think it needless to expatiate further on the matter.\nEuclidean space is not a form imposed upon our sensibility, since we can\nimagine non-Euclidean space; but the two spaces, Euclidean and\nnon-Euclidean, have a common basis, that amorphous continuum of which I\nspoke in the beginning. From this continuum we can get either Euclidean\nspace or Lobachevskian space, just as we can, by tracing upon it a\nproper graduation, transform an ungraduated thermometer into a\nFahrenheit or a R\u00e9aumur thermometer.\n\nAnd then comes a question: Is not this amorphous continuum, that our\nanalysis has allowed to survive, a form imposed upon our sensibility? If\nso, we should have enlarged the prison in which this sensibility is\nconfined, but it would always be a prison.\n\nThis continuum has a certain number of properties, exempt from all idea\nof measurement. The study of these properties is the object of a science\nwhich has been cultivated by many great geometers and in particular by\nRiemann and Betti and which has received the name of analysis situs. In\nthis science abstraction is made of every quantitative idea and, for\nexample, if we ascertain that on a line the point _B_ is between the\npoints _A_ and _C_, we shall be content with this ascertainment and\nshall not trouble to know whether the line _ABC_ is straight or curved,\nnor whether the length _AB_ is equal to the length _BC_, or whether it\nis twice as great.\n\nThe theorems of analysis situs have, therefore, this peculiarity, that\nthey would remain true if the figures were copied by an inexpert\ndraftsman who should grossly change all the proportions and replace the\nstraights by lines more or less sinuous. In mathematical terms, they are\nnot altered by any 'point-transformation' whatsoever. It has often been\nsaid that metric geometry was quantitative, while projective geometry\nwas purely qualitative. That is not altogether true. The straight is\nstill distinguished from other lines by properties which remain\nquantitative in some respects. The real qualitative geometry is,\ntherefore, analysis situs.\n\nThe same questions which came up apropos of the truths of Euclidean\ngeometry, come up anew apropos of the theorems of analysis situs. Are\nthey obtainable by deductive reasoning? Are they disguised conventions?\nAre they experimental verities? Are they the characteristics of a form\nimposed either upon our sensibility or upon our understanding?\n\nI wish simply to observe that the last two solutions exclude each other.\nWe can not admit at the same time that it is impossible to imagine space\nof four dimensions and that experience proves to us that space has three\ndimensions. The experimenter puts to nature a question: Is it this or\nthat? and he can not put it without imagining the two terms of the\nalternative. If it were impossible to imagine one of these terms, it\nwould be futile and besides impossible to consult experience. There is\nno need of observation to know that the hand of a watch is not marking\nthe hour 15 on the dial, because we know beforehand that there are only\n12, and we could not look at the mark 15 to see if the hand is there,\nbecause this mark does not exist.\n\nNote likewise that in analysis situs the empiricists are disembarrassed\nof one of the gravest objections that can be leveled against them, of\nthat which renders absolutely vain in advance all their efforts to apply\ntheir thesis to the verities of Euclidean geometry. These verities are\nrigorous and all experimentation can only be approximate. In analysis\nsitus approximate experiments may suffice to give a rigorous theorem\nand, for instance, if it is seen that space can not have either two or\nless than two dimensions, nor four or more than four, we are certain\nthat it has exactly three, since it could not have two and a half or\nthree and a half.\n\nOf all the theorems of analysis situs, the most important is that which\nis expressed in saying that space has three dimensions. This it is that\nwe are about to consider, and we shall put the question in these terms:\nWhen we say that space has three dimensions, what do we mean?\n\n\n3. _The Physical Continuum of Several Dimensions_\n\nI have explained in 'Science and Hypothesis' whence we derive the notion\nof physical continuity and how that of mathematical continuity has\narisen from it. It happens that we are capable of distinguishing two\nimpressions one from the other, while each is indistinguishable from a\nthird. Thus we can readily distinguish a weight of 12 grams from a\nweight of 10 grams, while a weight of 11 grams could be distinguished\nfrom neither the one nor the other. Such a statement, translated into\nsymbols, may be written:\n\n _A_ = _B_, _B_ = _C_, _A_ < _C_.\n\nThis would be the formula of the physical continuum, as crude experience\ngives it to us, whence arises an intolerable contradiction that has\nbeen obviated by the introduction of the mathematical continuum. This is\na scale of which the steps (commensurable or incommensurable numbers)\nare infinite in number but are exterior to one another, instead of\nencroaching on one another as do the elements of the physical continuum,\nin conformity with the preceding formula.\n\nThe physical continuum is, so to speak, a nebula not resolved; the most\nperfect instruments could not attain to its resolution. Doubtless if we\nmeasured the weights with a good balance instead of judging them by the\nhand, we could distinguish the weight of 11 grams from those of 10 and\n12 grams, and our formula would become:\n\n _A_ < _B_, _B_ < _C_, _A_ < _C_.\n\nBut we should always find between _A_ and _B_ and between _B_ and _C_\nnew elements _D_ and _E_, such that\n\n _A_ = _D_, _D_ = _B_, _A_ < _B_;\n _B_ = _E_, _E_ = _C_, _B_ < _C_,\n\nand the difficulty would only have receded and the nebula would always\nremain unresolved; the mind alone can resolve it and the mathematical\ncontinuum it is which is the nebula resolved into stars.\n\nYet up to this point we have not introduced the notion of the number of\ndimensions. What is meant when we say that a mathematical continuum or\nthat a physical continuum has two or three dimensions?\n\nFirst we must introduce the notion of cut, studying first physical\ncontinua. We have seen what characterizes the physical continuum. Each\nof the elements of this continuum consists of a manifold of impressions;\nand it may happen either that an element can not be discriminated from\nanother element of the same continuum, if this new element corresponds\nto a manifold of impressions not sufficiently different, or, on the\ncontrary, that the discrimination is possible; finally it may happen\nthat two elements indistinguishable from a third may, nevertheless, be\ndistinguished one from the other.\n\nThat postulated, if _A_ and _B_ are two distinguishable elements of a\ncontinuum _C_, a series of elements may be found, E_{1}, E_{2}, ...,\nE_{_n_}, all belonging to this same continuum _C_ and such that\neach of them is indistinguishable from the preceding, that E_{1} is\nindistinguishable from _A_, and E_{_n_} indistinguishable from _B_.\nTherefore we can go from _A_ to _B_ by a continuous route and without\nquitting _C_. If this condition is fulfilled for any two elements _A_\nand _B_ of the continuum _C_, we may say that this continuum _C_ is all\nin one piece. Now let us distinguish certain of the elements of _C_\nwhich may either be all distinguishable from one another, or themselves\nform one or several continua. The assemblage of the elements thus chosen\narbitrarily among all those of _C_ will form what I shall call the _cut_\nor the _cuts_.\n\nTake on _C_ any two elements _A_ and _B_. Either we can also find a\nseries of elements E_{1}, E_{2}, ..., E_{_n_}, such: (1) that they all\nbelong to _C_; (2) that each of them is indistinguishable from the\nfollowing, E_{1} indistinguishable from _A_ and E_{_n_} from _B_; (3)\n_and besides that none of the elements _E_ is indistinguishable from any\nelement of the cut_. Or else, on the contrary, in each of the series\nE_{1}, E_{2}, ..., E_{_n_} satisfying the first two conditions, there\nwill be an element _E_ indistinguishable from one of the elements of the\ncut. In the first case we can go from _A_ to _B_ by a continuous route\nwithout quitting _C_ and _without meeting the cuts_; in the second case\nthat is impossible.\n\nIf then for any two elements _A_ and _B_ of the continuum _C_, it is\nalways the first case which presents itself, we shall say that _C_\nremains all in one piece despite the cuts.\n\nThus, if we choose the cuts in a certain way, otherwise arbitrary, it\nmay happen either that the continuum remains all in one piece or that it\ndoes not remain all in one piece; in this latter hypothesis we shall\nthen say that it is _divided_ by the cuts.\n\nIt will be noticed that all these definitions are constructed in setting\nout solely from this very simple fact, that two manifolds of impressions\nsometimes can be discriminated, sometimes can not be. That postulated,\nif, to _divide_ a continuum, it suffices to consider as cuts a certain\nnumber of elements all distinguishable from one another, we say that\nthis continuum _is of one dimension_; if, on the contrary, to divide a\ncontinuum, it is necessary to consider as cuts a system of elements\nthemselves forming one or several continua, we shall say that this\ncontinuum is _of several dimensions_.\n\nIf to divide a continuum _C_, cuts forming one or several continua of\none dimension suffice, we shall say that _C_ is a continuum _of two\ndimensions_; if cuts suffice which form one or several continua of two\ndimensions at most, we shall say that _C_ is a continuum _of three\ndimensions_; and so on.\n\nTo justify this definition it is proper to see whether it is in this way\nthat geometers introduce the notion of three dimensions at the beginning\nof their works. Now, what do we see? Usually they begin by defining\nsurfaces as the boundaries of solids or pieces of space, lines as the\nboundaries of surfaces, points as the boundaries of lines, and they\naffirm that the same procedure can not be pushed further.\n\nThis is just the idea given above: to divide space, cuts that are called\nsurfaces are necessary; to divide surfaces, cuts that are called lines\nare necessary; to divide lines, cuts that are called points are\nnecessary; we can go no further, the point can not be divided, so the\npoint is not a continuum. Then lines which can be divided by cuts which\nare not continua will be continua of one dimension; surfaces which can\nbe divided by continuous cuts of one dimension will be continua of two\ndimensions; finally, space which can be divided by continuous cuts of\ntwo dimensions will be a continuum of three dimensions.\n\nThus the definition I have just given does not differ essentially from\nthe usual definitions; I have only endeavored to give it a form\napplicable not to the mathematical continuum, but to the physical\ncontinuum, which alone is susceptible of representation, and yet to\nretain all its precision. Moreover, we see that this definition applies\nnot alone to space; that in all which falls under our senses we find the\ncharacteristics of the physical continuum, which would allow of the same\nclassification; that it would be easy to find there examples of continua\nof four, of five, dimensions, in the sense of the preceding definition;\nsuch examples occur of themselves to the mind.\n\nI should explain finally, if I had the time, that this science, of which\nI spoke above and to which Riemann gave the name of analysis situs,\nteaches us to make distinctions among continua of the same number of\ndimensions and that the classification of these continua rests also on\nthe consideration of cuts.\n\nFrom this notion has arisen that of the mathematical continuum of\nseveral dimensions in the same way that the physical continuum of one\ndimension engendered the mathematical continuum of one dimension. The\nformula\n\n _A_ > _C_, _A_ = _B_, _B_ = _C_,\n\nwhich summed up the data of crude experience, implied an intolerable\ncontradiction. To get free from it, it was necessary to introduce a new\nnotion while still respecting the essential characteristics of the\nphysical continuum of several dimensions. The mathematical continuum of\none dimension admitted of a scale whose divisions, infinite in number,\ncorresponded to the different values, commensurable or not, of one same\nmagnitude. To have the mathematical continuum of _n_ dimensions, it will\nsuffice to take _n_ like scales whose divisions correspond to different\nvalues of _n_ independent magnitudes called coordinates. We thus shall\nhave an image of the physical continuum of _n_ dimensions, and this\nimage will be as faithful as it can be after the determination not to\nallow the contradiction of which I spoke above.\n\n\n4. _The Notion of Point_\n\nIt seems now that the question we put to ourselves at the start is\nanswered. When we say that space has three dimensions, it will be said,\nwe mean that the manifold of points of space satisfies the definition we\nhave just given of the physical continuum of three dimensions. To be\ncontent with that would be to suppose that we know what is the manifold\nof points of space, or even one point of space.\n\nNow that is not as simple as one might think. Every one believes he\nknows what a point is, and it is just because we know it too well that\nwe think there is no need of defining it. Surely we can not be required\nto know how to define it, because in going back from definition to\ndefinition a time must come when we must stop. But at what moment should\nwe stop?\n\nWe shall stop first when we reach an object which falls under our senses\nor that we can represent to ourselves; definition then will become\nuseless; we do not define the sheep to a child; we say to him: _See_ the\nsheep.\n\nSo, then, we should ask ourselves if it is possible to represent to\nourselves a point of space. Those who answer yes do not reflect that\nthey represent to themselves in reality a white spot made with the chalk\non a blackboard or a black spot made with a pen on white paper, and that\nthey can represent to themselves only an object or rather the\nimpressions that this object made on their senses.\n\nWhen they try to represent to themselves a point, they represent the\nimpressions that very little objects made them feel. It is needless to\nadd that two different objects, though both very little, may produce\nextremely different impressions, but I shall not dwell on this\ndifficulty, which would still require some discussion.\n\nBut it is not a question of that; it does not suffice to represent _one_\npoint, it is necessary to represent _a certain_ point and to have the\nmeans of distinguishing it from an _other_ point. And in fact, that we\nmay be able to apply to a continuum the rule I have above expounded and\nby which one may recognize the number of its dimensions, we must rely\nupon the fact that two elements of this continuum sometimes can and\nsometimes can not be distinguished. It is necessary therefore that we\nshould in certain cases know how to represent to ourselves _a specific_\nelement and to distinguish it from an _other_ element.\n\nThe question is to know whether the point that I represented to myself\nan hour ago is the same as this that I now represent to myself, or\nwhether it is a different point. In other words, how do we know whether\nthe point occupied by the object _A_ at the instant [alpha] is the same\nas the point occupied by the object _B_ at the instant [beta], or still\nbetter, what this means?\n\nI am seated in my room; an object is placed on my table; during a second\nI do not move, no one touches the object. I am tempted to say that the\npoint _A_ which this object occupied at the beginning of this second is\nidentical with the point _B_ which it occupies at its end. Not at all;\nfrom the point _A_ to the point _B_ is 30 kilometers, because the object\nhas been carried along in the motion of the earth. We can not know\nwhether an object, be it large or small, has not changed its absolute\nposition in space, and not only can we not affirm it, but this\naffirmation has no meaning and in any case can not correspond to any\nrepresentation.\n\nBut then we may ask ourselves if the relative position of an object with\nregard to other objects has changed or not, and first whether the\nrelative position of this object with regard to our body has changed. If\nthe impressions this object makes upon us have not changed, we shall be\ninclined to judge that neither has this relative position changed; if\nthey have changed, we shall judge that this object has changed either in\nstate or in relative position. It remains to decide which of the _two_.\nI have explained in 'Science and Hypothesis' how we have been led to\ndistinguish the changes of position. Moreover, I shall return to that\nfurther on. We come to know, therefore, whether the relative position of\nan object with regard to our body has or has not remained the same.\n\nIf now we see that two objects have retained their relative position\nwith regard to our body, we conclude that the relative position of these\ntwo objects with regard to one another has not changed; but we reach\nthis conclusion only by indirect reasoning. The only thing that we know\ndirectly is the relative position of the objects with regard to our\nbody. _A fortiori_ it is only by indirect reasoning that we think we\nknow (and, moreover, this belief is delusive) whether the absolute\nposition of the object has changed.\n\nIn a word, the system of coordinate axes to which we naturally refer all\nexterior objects is a system of axes invariably bound to our body, and\ncarried around with us.\n\nIt is impossible to represent to oneself absolute space; when I try to\nrepresent to myself simultaneously objects and myself in motion in\nabsolute space, in reality I represent to myself my own self motionless\nand seeing move around me different objects and a man that is exterior\nto me, but that I convene to call me.\n\nWill the difficulty be solved if we agree to refer everything to these\naxes bound to our body? Shall we know then what is a point thus defined\nby its relative position with regard to ourselves? Many persons will\nanswer yes and will say that they 'localize' exterior objects.\n\nWhat does this mean? To localize an object simply means to represent to\noneself the movements that would be necessary to reach it. I will\nexplain myself. It is not a question of representing the movements\nthemselves in space, but solely of representing to oneself the muscular\nsensations which accompany these movements and which do not presuppose\nthe preexistence of the notion of space.\n\nIf we suppose two different objects which successively occupy the same\nrelative position with regard to ourselves, the impressions that these\ntwo objects make upon us will be very different; if we localize them at\nthe same point, this is simply because it is necessary to make the same\nmovements to reach them; apart from that, one can not just see what they\ncould have in common.\n\nBut, given an object, we can conceive many different series of movements\nwhich equally enable us to reach it. If then we represent to ourselves a\npoint by representing to ourselves the series of muscular sensations\nwhich accompany the movements which enable us to reach this point, there\nwill be many ways entirely different of representing to oneself the same\npoint. If one is not satisfied with this solution, but wishes, for\ninstance, to bring in the visual sensations along with the muscular\nsensations, there will be one or two more ways of representing to\noneself this same point and the difficulty will only be increased. In\nany case the following question comes up: Why do we think that all these\nrepresentations so different from one another still represent the same\npoint?\n\nAnother remark: I have just said that it is to our own body that we\nnaturally refer exterior objects; that we carry about everywhere with us\na system of axes to which we refer all the points of space and that this\nsystem of axes seems to be invariably bound to our body. It should be\nnoticed that rigorously we could not speak of axes invariably bound to\nthe body unless the different parts of this body were themselves\ninvariably bound to one another. As this is not the case, we ought,\nbefore referring exterior objects to these fictitious axes, to suppose\nour body brought back to the initial attitude.\n\n\n5. _The Notion of Displacement_\n\nI have shown in 'Science and Hypothesis' the preponderant r\u00f4le played by\nthe movements of our body in the genesis of the notion of space. For a\nbeing completely immovable there would be neither space nor geometry; in\nvain would exterior objects be displaced about him, the variations which\nthese displacements would make in his impressions would not be\nattributed by this being to changes of position, but to simple changes\nof state; this being would have no means of distinguishing these two\nsorts of changes, and this distinction, fundamental for us, would have\nno meaning for him.\n\nThe movements that we impress upon our members have as effect the\nvarying of the impressions produced on our senses by external objects;\nother causes may likewise make them vary; but we are led to distinguish\nthe changes produced by our own motions and we easily discriminate them\nfor two reasons: (1) because they are voluntary; (2) because they are\naccompanied by muscular sensations.\n\nSo we naturally divide the changes that our impressions may undergo into\ntwo categories to which perhaps I have given an inappropriate\ndesignation: (1) the internal changes, which are voluntary and\naccompanied by muscular sensations; (2) the external changes, having the\nopposite characteristics.\n\nWe then observe that among the external changes are some which can be\ncorrected, thanks to an internal change which brings everything back to\nthe primitive state; others can not be corrected in this way (it is thus\nthat, when an exterior object is displaced, we may then by changing our\nown position replace ourselves as regards this object in the same\nrelative position as before, so as to reestablish the original aggregate\nof impressions; if this object was not displaced, but changed its state,\nthat is impossible). Thence comes a new distinction among external\nchanges: those which may be so corrected we call changes of position;\nand the others, changes of state.\n\nThink, for example, of a sphere with one hemisphere blue and the other\nred; it first presents to us the blue hemisphere, then it so revolves as\nto present the red hemisphere. Now think of a spherical vase containing\na blue liquid which becomes red in consequence of a chemical reaction.\nIn both cases the sensation of red has replaced that of blue; our senses\nhave experienced the same impressions which have succeeded each other in\nthe same order, and yet these two changes are regarded by us as very\ndifferent; the first is a displacement, the second a change of state.\nWhy? Because in the first case it is sufficient for me to go around the\nsphere to place myself opposite the blue hemisphere and reestablish the\noriginal blue sensation.\n\nStill more; if the two hemispheres, in place of being red and blue, had\nbeen yellow and green, how should I have interpreted the revolution of\nthe sphere? Before, the red succeeded the blue, now the green succeeds\nthe yellow; and yet I say that the two spheres have undergone the same\nrevolution, that each has turned about its axis; yet I can not say that\nthe green is to yellow as the red is to blue; how then am I led to\ndecide that the two spheres have undergone the _same_ displacement?\nEvidently because, in one case as in the other, I am able to reestablish\nthe original sensation by going around the sphere, by making the same\nmovements, and I know that I have made the same movements because I have\nfelt the same muscular sensations; to know it, I do not need, therefore,\nto know geometry in advance and to represent to myself the movements of\nmy body in geometric space.\n\nAnother example: An object is displaced before my eye; its image was\nfirst formed at the center of the retina; then it is formed at the\nborder; the old sensation was carried to me by a nerve fiber ending at\nthe center of the retina; the new sensation is carried to me by\n_another_ nerve fiber starting from the border of the retina; these two\nsensations are qualitatively different; otherwise, how could I\ndistinguish them?\n\nWhy then am I led to decide that these two sensations, qualitatively\ndifferent, represent the same image, which has been displaced? It is\nbecause I _can follow the object with the eye_ and by a displacement of\nthe eye, voluntary and accompanied by muscular sensations, bring back\nthe image to the center of the retina and reestablish the primitive\nsensation.\n\nI suppose that the image of a red object has gone from the center _A_ to\nthe border _B_ of the retina, then that the image of a blue object goes\nin its turn from the center _A_ to the border _B_ of the retina; I shall\ndecide that these two objects have undergone the _same_ displacement.\nWhy? Because in both cases I shall have been able to reestablish the\nprimitive sensation, and that to do it I shall have had to execute the\n_same_ movement of the eye, and I shall know that my eye has executed\nthe same movement because I shall have felt the _same_ muscular\nsensations.\n\nIf I could not move my eye, should I have any reason to suppose that the\nsensation of red at the center of the retina is to the sensation of red\nat the border of the retina as that of blue at the center is to that of\nblue at the border? I should only have four sensations qualitatively\ndifferent, and if I were asked if they are connected by the proportion I\nhave just stated, the question would seem to me ridiculous, just as if I\nwere asked if there is an analogous proportion between an auditory\nsensation, a tactile sensation and an olfactory sensation.\n\nLet us now consider the internal changes, that is, those which are\nproduced by the voluntary movements of our body and which are\naccompanied by muscular changes. They give rise to the two following\nobservations, analogous to those we have just made on the subject of\nexternal changes.\n\n1. I may suppose that my body has moved from one point to another, but\nthat the same _attitude_ is retained; all the parts of the body have\ntherefore retained or resumed the same _relative_ situation, although\ntheir absolute situation in space may have varied. I may suppose that\nnot only has the position of my body changed, but that its attitude is\nno longer the same, that, for instance, my arms which before were folded\nare now stretched out.\n\nI should therefore distinguish the simple changes of position without\nchange of attitude, and the changes of attitude. Both would appear to me\nunder form of muscular sensations. How then am I led to distinguish\nthem? It is that the first may serve to correct an external change, and\nthat the others can not, or at least can only give an imperfect\ncorrection.\n\nThis fact I proceed to explain as I would explain it to some one who\nalready knew geometry, but it need not thence be concluded that it is\nnecessary already to know geometry to make this distinction; before\nknowing geometry I ascertain the fact (experimentally, so to speak),\nwithout being able to explain it. But merely to make the distinction\nbetween the two kinds of change, I do not need to _explain_ the fact, it\nsuffices me _to ascertain_ it.\n\nHowever that may be, the explanation is easy. Suppose that an exterior\nobject is displaced; if we wish the different parts of our body to\nresume with regard to this object their initial relative position, it is\nnecessary that these different parts should have resumed likewise their\ninitial relative position with regard to one another. Only the internal\nchanges which satisfy this latter condition will be capable of\ncorrecting the external change produced by the displacement of that\nobject. If, therefore, the relative position of my eye with regard to my\nfinger has changed, I shall still be able to replace the eye in its\ninitial relative situation with regard to the object and reestablish\nthus the primitive visual sensations, but then the relative position of\nthe finger with regard to the object will have changed and the tactile\nsensations will not be reestablished.\n\n2. We ascertain likewise that the same external change may be corrected\nby two internal changes corresponding to different muscular sensations.\nHere again I can ascertain this without knowing geometry; and I have no\nneed of anything else; but I proceed to give the explanation of the\nfact, employing geometrical language. To go from the position _A_ to the\nposition _B_ I may take several routes. To the first of these routes\nwill correspond a series _S_ of muscular sensations; to a second route\nwill correspond another series _S''_, of muscular sensations which\ngenerally will be completely different, since other muscles will be\nused.\n\nHow am I led to regard these two series _S_ and _S''_ as corresponding\nto the same displacement _AB_? It is because these two series are\ncapable of correcting the same external change. Apart from that, they\nhave nothing in common.\n\nLet us now consider two external changes: [alpha] and [beta], which\nshall be, for instance, the rotation of a sphere half blue, half red,\nand that of a sphere half yellow, half green; these two changes have\nnothing in common, since the one is for us the passing of blue into red\nand the other the passing of yellow into green. Consider, on the other\nhand, two series of internal changes _S_ and _S''_; like the others,\nthey will have nothing in common. And yet I say that [alpha] and [beta]\ncorrespond to the same displacement, and that _S_ and _S''_ correspond\nalso to the same displacement. Why? Simply because _S_ can correct\n[alpha] as well as [beta] and because [alpha] can be corrected by _S''_\nas well as by _S_. And then a question suggests itself:\n\nIf I have ascertained that _S_ corrects [alpha] and [beta] and that\n_S''_ corrects [alpha], am I certain that _S''_ likewise corrects\n[beta]? Experiment alone can teach us whether this law is verified. If\nit were not verified, at least approximately, there would be no\ngeometry, there would be no space, because we should have no more\ninterest in classifying the internal and external changes as I have just\ndone, and, for instance, in distinguishing changes of state from changes\nof position.\n\nIt is interesting to see what has been the r\u00f4le of experience in all\nthis. It has shown me that a certain law is approximately verified. It\nhas not told me _how_ space is, and that it satisfies the condition in\nquestion. I knew, in fact, before all experience, that space satisfied\nthis condition or that it would not be; nor have I any right to say that\nexperience told me that geometry is possible; I very well see that\ngeometry is possible, since it does not imply contradiction; experience\nonly tells me that geometry is useful.\n\n\n6. _Visual Space_\n\nAlthough motor impressions have had, as I have just explained, an\naltogether preponderant influence in the genesis of the notion of space,\nwhich never would have taken birth without them, it will not be without\ninterest to examine also the r\u00f4le of visual impressions and to\ninvestigate how many dimensions 'visual space' has, and for that purpose\nto apply to these impressions the definition of \u00a7 3.\n\nA first difficulty presents itself: consider a red color sensation\naffecting a certain point of the retina; and on the other hand a blue\ncolor sensation affecting the same point of the retina. It is necessary\nthat we have some means of recognizing that these two sensations,\nqualitatively different, have something in common. Now, according to the\nconsiderations expounded in the preceding paragraph, we have been able\nto recognize this only by the movements of the eye and the observations\nto which they have given rise. If the eye were immovable, or if we were\nunconscious of its movements, we should not have been able to recognize\nthat these two sensations, of different quality, had something in\ncommon; we should not have been able to disengage from them what gives\nthem a geometric character. The visual sensations, without the muscular\nsensations, would have nothing geometric, so that it may be said there\nis no pure visual space.\n\nTo do away with this difficulty, consider only sensations of the same\nnature, red sensations, for instance, differing one from another only as\nregards the point of the retina that they affect. It is clear that I\nhave no reason for making such an arbitrary choice among all the\npossible visual sensations, for the purpose of uniting in the same class\nall the sensations of the same color, whatever may be the point of the\nretina affected. I should never have dreamt of it, had I not before\nlearned, by the means we have just seen, to distinguish changes of state\nfrom changes of position, that is, if my eye were immovable. Two\nsensations of the same color affecting two different parts of the retina\nwould have appeared to me as qualitatively distinct, just as two\nsensations of different color.\n\nIn restricting myself to red sensations, I therefore impose upon myself\nan artificial limitation and I neglect systematically one whole side of\nthe question; but it is only by this artifice that I am able to analyze\nvisual space without mingling any motor sensation.\n\nImagine a line traced on the retina and dividing in two its surface; and\nset apart the red sensations affecting a point of this line, or those\ndiffering from them too little to be distinguished from them. The\naggregate of these sensations will form a sort of cut that I shall call\n_C_, and it is clear that this cut suffices to divide the manifold of\npossible red sensations, and that if I take two red sensations affecting\ntwo points situated on one side and the other of the line, I can not\npass from one of these sensations to the other in a continuous way\nwithout passing at a certain moment through a sensation belonging to the\ncut.\n\nIf, therefore, the cut has _n_ dimensions, the total manifold of my red\nsensations, or if you wish, the whole visual space, will have _n_ + 1.\n\nNow, I distinguish the red sensations affecting a point of the cut _C_.\nThe assemblage of these sensations will form a new cut _C'_. It is clear\nthat this will divide the cut _C_, always giving to the word divide the\nsame meaning.\n\nIf, therefore, the cut _C'_ has _n_ dimensions, the cut _C_ will have\n_n_ + 1 and the whole of visual space _n_ + 2.\n\nIf all the red sensations affecting the same point of the retina were\nregarded as identical, the cut _C'_ reducing to a single element would\nhave 0 dimensions, and visual space would have 2.\n\nAnd yet most often it is said that the eye gives us the sense of a third\ndimension, and enables us in a certain measure to recognize the distance\nof objects. When we seek to analyze this feeling, we ascertain that it\nreduces either to the consciousness of the convergence of the eyes, or\nto that of the effort of accommodation which the ciliary muscle makes to\nfocus the image.\n\nTwo red sensations affecting the same point of the retina will therefore\nbe regarded as identical only if they are accompanied by the same\nsensation of convergence and also by the same sensation of effort of\naccommodation or at least by sensations of convergence and accommodation\nso slightly different as to be indistinguishable.\n\nOn this account the cut _C'_ is itself a continuum and the cut _C_ has\nmore than one dimension.\n\nBut it happens precisely that experience teaches us that when two visual\nsensations are accompanied by the same sensation of convergence, they\nare likewise accompanied by the same sensation of accommodation. If then\nwe form a new cut _C''_ with all those of the sensations of the cut\n_C'_, which are accompanied by a certain sensation of convergence, in\naccordance with the preceding law they will all be indistinguishable and\nmay be regarded as identical. Therefore _C''_ will not be a continuum\nand will have 0 dimension; and as _C''_ divides _C'_ it will thence\nresult that _C'_ has one, _C_ two and _the whole visual space three\ndimensions_.\n\nBut would it be the same if experience had taught us the contrary and if\na certain sensation of convergence were not always accompanied by the\nsame sensation of accommodation? In this case two sensations affecting\nthe same point of the retina and accompanied by the same sense of\nconvergence, two sensations which consequently would both appertain to\nthe cut _C''_, could nevertheless be distinguished since they would be\naccompanied by two different sensations of accommodation. Therefore\n_C''_ would be in its turn a continuum and would have one dimension (at\nleast); then _C'_ would have two, _C_ three and _the whole visual space\nwould have four dimensions_.\n\nWill it then be said that it is experience which teaches us that space\nhas three dimensions, since it is in setting out from an experimental\nlaw that we have come to attribute three to it? But we have therein\nperformed, so to speak, only an experiment in physiology; and as also it\nwould suffice to fit over the eyes glasses of suitable construction to\nput an end to the accord between the feelings of convergence and of\naccommodation, are we to say that putting on spectacles is enough to\nmake space have four dimensions and that the optician who constructed\nthem has given one more dimension to space? Evidently not; all we can\nsay is that experience has taught us that it is convenient to attribute\nthree dimensions to space.\n\nBut visual space is only one part of space, and in even the notion of\nthis space there is something artificial, as I have explained at the\nbeginning. The real space is motor space and this it is that we shall\nexamine in the following chapter.\n\n\n\n\nCHAPTER IV\n\nSPACE AND ITS THREE DIMENSIONS\n\n\n1. _The Group of Displacements_\n\nLet us sum up briefly the results obtained. We proposed to investigate\nwhat was meant in saying that space has three dimensions and we have\nasked first what is a physical continuum and when it may be said to have\n_n_ dimensions. If we consider different systems of impressions and\ncompare them with one another, we often recognize that two of these\nsystems of impressions are indistinguishable (which is ordinarily\nexpressed in saying that they are too close to one another, and that our\nsenses are too crude, for us to distinguish them) and we ascertain\nbesides that two of these systems can sometimes be discriminated from\none another though indistinguishable from a third system. In that case\nwe say the manifold of these systems of impressions forms a physical\ncontinuum _C_. And each of these systems is called an _element_ of the\ncontinuum _C_.\n\nHow many dimensions has this continuum? Take first two elements _A_ and\n_B_ of _C_, and suppose there exists a series [Sigma] of elements, all\nbelonging to the continuum _C_, of such a sort that _A_ and _B_ are the\ntwo extreme terms of this series and that each term of the series is\nindistinguishable from the preceding. If such a series [Sigma] can be\nfound, we say that _A_ and _B_ are joined to one another; and if any two\nelements of _C_ are joined to one another, we say that _C_ is all of one\npiece.\n\nNow take on the continuum _C_ a certain number of elements in a way\naltogether arbitrary. The aggregate of these elements will be called a\n_cut_. Among the various series [Sigma] which join _A_ to _B_, we shall\ndistinguish those of which an element is indistinguishable from one of\nthe elements of the cut (we shall say that these are they which _cut_\nthe cut) and those of which _all_ the elements are distinguishable from\nall those of the cut. If _all_ the series [Sigma] which join _A_ to _B_\ncut the cut, we shall say that _A_ and _B_ are _separated_ by the cut,\nand that the cut _divides_ _C_. If we can not find on _C_ two elements\nwhich are separated by the cut, we shall say that the cut _does not\ndivide_ _C_.\n\nThese definitions laid down, if the continuum _C_ can be divided by cuts\nwhich do not themselves form a continuum, this continuum _C_ has only\none dimension; in the contrary case it has several. If a cut forming a\ncontinuum of 1 dimension suffices to divide _C_, _C_ will have 2\ndimensions; if a cut forming a continuum of 2 dimensions suffices, _C_\nwill have 3 dimensions, etc. Thanks to these definitions, we can always\nrecognize how many dimensions any physical continuum has. It only\nremains to find a physical continuum which is, so to speak, equivalent\nto space, of such a sort that to every point of space corresponds an\nelement of this continuum, and that to points of space very near one\nanother correspond indistinguishable elements. Space will have then as\nmany dimensions as this continuum.\n\nThe intermediation of this physical continuum, capable of\nrepresentation, is indispensable; because we can not represent space to\nourselves, and that for a multitude of reasons. Space is a mathematical\ncontinuum, it is infinite, and we can represent to ourselves only\nphysical continua and finite objects. The different elements of space,\nwhich we call points, are all alike, and, to apply our definition, it is\nnecessary that we know how to distinguish the elements from one another,\nat least if they are not too close. Finally absolute space is nonsense,\nand it is necessary for us to begin by referring space to a system of\naxes invariably bound to our body (which we must always suppose put back\nin the initial attitude).\n\nThen I have sought to form with our visual sensations a physical\ncontinuum equivalent to space; that certainly is easy and this example\nis particularly appropriate for the discussion of the number of\ndimensions; this discussion has enabled us to see in what measure it is\nallowable to say that 'visual space' has three dimensions. Only this\nsolution is incomplete and artificial. I have explained why, and it is\nnot on visual space but on motor space that it is necessary to bring our\nefforts to bear. I have then recalled what is the origin of the\ndistinction we make between changes of position and changes of state.\nAmong the changes which occur in our impressions, we distinguish, first\nthe _internal_ changes, voluntary and accompanied by muscular\nsensations, and the _external_ changes, having opposite characteristics.\nWe ascertain that it may happen that an external change may be\n_corrected_ by an internal change which reestablishes the primitive\nsensations. The external changes, capable of being corrected by an\ninternal change are called _changes of position_, those not capable of\nit are called _changes of state_. The internal changes capable of\ncorrecting an external change are called _displacements of the whole\nbody_; the others are called _changes of attitude_.\n\nNow let [alpha] and [beta] be two external changes, [alpha]' and [beta]'\ntwo internal changes. Suppose that a may be corrected either by [alpha]'\nor by [beta]', and that [alpha]' can correct either [alpha] or [beta];\nexperience tells us then that [beta]' can likewise correct [beta]. In\nthis case we say that [alpha] and [beta] correspond to the _same_\ndisplacement and also that [alpha]' and [beta]' correspond to the _same_\ndisplacement. That postulated, we can imagine a physical continuum which\nwe shall call _the continuum or group of displacements_ and which we\nshall define in the following manner. The elements of this continuum\nshall be the internal changes capable of correcting an external change.\nTwo of these internal changes [alpha]' and [beta]' shall be regarded as\nindistinguishable: (1) if they are so naturally, that is, if they are\ntoo close to one another; (2) if [alpha]' is capable of correcting the\nsame external change as a third internal change naturally\nindistinguishable from [beta]'. In this second case, they will be, so to\nspeak, indistinguishable by convention, I mean by agreeing to disregard\ncircumstances which might distinguish them.\n\nOur continuum is now entirely defined, since we know its elements and\nhave fixed under what conditions they may be regarded as\nindistinguishable. We thus have all that is necessary to apply our\ndefinition and determine how many dimensions this continuum has. We\nshall recognize that it has _six_. The continuum of displacements is,\ntherefore, not equivalent to space, since the number of dimensions is\nnot the same; it is only related to space. Now how do we know that this\ncontinuum of displacements has six dimensions? We know it _by\nexperience_.\n\nIt would be easy to describe the experiments by which we could arrive\nat this result. It would be seen that in this continuum cuts can be made\nwhich divide it and which are continua; that these cuts themselves can\nbe divided by other cuts of the second order which yet are continua, and\nthat this would stop only after cuts of the sixth order which would no\nlonger be continua. From our definitions that would mean that the group\nof displacements has six dimensions.\n\nThat would be easy, I have said, but that would be rather long; and\nwould it not be a little superficial? This group of displacements, we\nhave seen, is related to space, and space could be deduced from it, but\nit is not equivalent to space, since it has not the same number of\ndimensions; and when we shall have shown how the notion of this\ncontinuum can be formed and how that of space may be deduced from it, it\nmight always be asked why space of three dimensions is much more\nfamiliar to us than this continuum of six dimensions, and consequently\ndoubted whether it was by this detour that the notion of space was\nformed in the human mind.\n\n\n2. _Identity of Two Points_\n\nWhat is a point? How do we know whether two points of space are\nidentical or different? Or, in other words, when I say: The object _A_\noccupied at the instant [alpha] the point which the object _B_ occupies\nat the instant [beta], what does that mean?\n\nSuch is the problem we set ourselves in the preceding chapter, \u00a74. As I\nhave explained it, it is not a question of comparing the positions of\nthe objects _A_ and _B_ in absolute space; the question then would\nmanifestly have no meaning. It is a question of comparing the positions\nof these two objects with regard to axes invariably bound to my body,\nsupposing always this body replaced in the same attitude.\n\nI suppose that between the instants [alpha] and [beta] I have moved\nneither my body nor my eye, as I know from my muscular sense. Nor have I\nmoved either my head, my arm or my hand. I ascertain that at the instant\n[alpha] impressions that I attributed to the object _A_ were transmitted\nto me, some by one of the fibers of my optic nerve, the others by one of\nthe sensitive tactile nerves of my finger; I ascertain that at the\ninstant [beta] other impressions which I attribute to the object _B_ are\ntransmitted to me, some by this same fiber of the optic nerve, the\nothers by this same tactile nerve.\n\nHere I must pause for an explanation; how am I told that this impression\nwhich I attribute to _A_, and that which I attribute to _B_, impressions\nwhich are qualitatively different, are transmitted to me by the same\nnerve? Must we suppose, to take for example the visual sensations, that\n_A_ produces two simultaneous sensations, a sensation purely luminous\n_a_ and a colored sensation _a'_, that _B_ produces in the same way\nsimultaneously a luminous sensation _b_ and a colored sensation _b'_,\nthat if these different sensations are transmitted to me by the same\nretinal fiber, _a_ is identical with _b_, but that in general the\ncolored sensations _a'_ and _b'_ produced by different bodies are\ndifferent? In that case it would be the identity of the sensation _a_\nwhich accompanies _a'_ with the sensation _b_ which accompanies _b'_,\nwhich would tell that all these sensations are transmitted to me by the\nsame fiber.\n\nHowever it may be with this hypothesis and although I am led to prefer\nto it others considerably more complicated, it is certain that we are\ntold in some way that there is something in common between these\nsensations _a_ + _a'_ and _b_ +_b'_, without which we should have no\nmeans of recognizing that the object _B_ has taken the place of the\nobject _A_.\n\nTherefore I do not further insist and I recall the hypothesis I have\njust made: I suppose that I have ascertained that the impressions which\nI attribute to _B_ are transmitted to me at the instant [beta] by the\nsame fibers, optic as well as tactile, which, at the instant [alpha],\nhad transmitted to me the impressions that I attributed to _A_. If it is\nso, we shall not hesitate to declare that the point occupied by _B_ at\nthe instant [beta] is identical with the point occupied by _A_ at the\ninstant [alpha].\n\nI have just enunciated two conditions for these points being identical;\none is relative to sight, the other to touch. Let us consider them\nseparately. The first is necessary, but is not sufficient. The second is\nat once necessary and sufficient. A person knowing geometry could easily\nexplain this in the following manner: Let _O_ be the point of the retina\nwhere is formed at the instant [alpha] the image of the body _A_; let\n_M_ be the point of space occupied at the instant [alpha] by this body\n_A_; let _M'_ be the point of space occupied at the instant [beta] by\nthe body _B_. For this body _B_ to form its image in _O_, it is not\nnecessary that the points _M_ and _M'_ coincide; since vision acts at a\ndistance, it suffices for the three points _O_ _M_ _M'_ to be in a\nstraight line. This condition that the two objects form their image on\n_O_ is therefore necessary, but not sufficient for the points _M_ and\n_M'_ to coincide. Let now _P_ be the point occupied by my finger and\nwhere it remains, since it does not budge. As touch does not act at a\ndistance, if the body _A_ touches my finger at the instant [alpha], it\nis because _M_ and _P_ coincide; if _B_ touches my finger at the instant\n[beta], it is because _M'_ and _P_ coincide. Therefore _M_ and _M'_\ncoincide. Thus this condition that if _A_ touches my finger at the\ninstant [alpha], _B_ touches it at the instant [beta], is at once\nnecessary and sufficient for _M_ and _M'_ to coincide.\n\nBut we who, as yet, do not know geometry can not reason thus; all that\nwe can do is to ascertain experimentally that the first condition\nrelative to sight may be fulfilled without the second, which is relative\nto touch, but that the second can not be fulfilled without the first.\n\nSuppose experience had taught us the contrary, as might well be; this\nhypothesis contains nothing absurd. Suppose, therefore, that we had\nascertained experimentally that the condition relative to touch may be\nfulfilled without that of sight being fulfilled and that, on the\ncontrary, that of sight can not be fulfilled without that of touch being\nalso. It is clear that if this were so we should conclude that it is\ntouch which may be exercised at a distance, and that sight does not\noperate at a distance.\n\nBut this is not all; up to this time I have supposed that to determine\nthe place of an object I have made use only of my eye and a single\nfinger; but I could just as well have employed other means, for example,\nall my other fingers.\n\nI suppose that my first finger receives at the instant [alpha] a tactile\nimpression which I attribute to the object _A_. I make a series of\nmovements, corresponding to a series _S_ of muscular sensations. After\nthese movements, at the instant [alpha]', my _second_ finger receives a\ntactile impression that I attribute likewise to _A_. Afterward, at the\ninstant [beta], without my having budged, as my muscular sense tells me,\nthis same second finger transmits to me anew a tactile impression which\nI attribute this time to the object _B_; I then make a series of\nmovements, corresponding to a series _S'_ of muscular sensations. I know\nthat this series _S'_ is the inverse of the series _S_ and corresponds\nto contrary movements. I know this because many previous experiences\nhave shown me that if I made successively the two series of movements\ncorresponding to _S_ and to _S'_, the primitive impressions would be\nreestablished, in other words, that the two series mutually compensate.\nThat settled, should I expect that at the instant [beta]', when the\nsecond series of movements is ended, my _first finger_ would feel a\ntactile impression attributable to the object _B_?\n\nTo answer this question, those already knowing geometry would reason as\nfollows: There are chances that the object _A_ has not budged, between\nthe instants [alpha] and [alpha]', nor the object _B_ between the\ninstants [beta] and [beta]'; assume this. At the instant [alpha], the\nobject _A_ occupied a certain point _M_ of space. Now at this instant it\ntouched my first finger, and _as touch does not operate at a distance_,\nmy first finger was likewise at the point _M_. I afterward made the\nseries _S_ of movements and at the end of this series, at the instant\n[alpha]', I ascertained that the object _A_ touched my second finger. I\nthence conclude that this second finger was then at _M_, that is, that\nthe movements _S_ had the result of bringing the second finger to the\nplace of the first. At the instant [beta] the object _B_ has come in\ncontact with my second finger: as I have not budged, this second finger\nhas remained at _M_; therefore the object _B_ has come to _M_; by\nhypothesis it does not budge up to the instant [beta]'. But between the\ninstants [beta] and [beta]' I have made the movements _S'_; as these\nmovements are the inverse of the movements _S_, they must have for\neffect bringing the first finger in the place of the second. At the\ninstant [beta]' this first finger will, therefore, be at _M_; and as the\nobject _B_ is likewise at _M_, this object _B_ will touch my first\nfinger. To the question put, the answer should therefore be yes.\n\nWe who do not yet know geometry can not reason thus; but we ascertain\nthat this anticipation is ordinarily realized; and we can always explain\nthe exceptions by saying that the object _A_ has moved between the\ninstants [alpha] and [alpha]', or the object _B_ between the instants\n[beta] and [beta]'.\n\nBut could not experience have given a contrary result? Would this\ncontrary result have been absurd in itself? Evidently not. What should\nwe have done then if experience had given this contrary result? Would\nall geometry thus have become impossible? Not the least in the world. We\nshould have contented ourselves with concluding _that touch can operate\nat a distance_.\n\nWhen I say, touch does not operate at a distance, but sight operates at\na distance, this assertion has only one meaning, which is as follows: To\nrecognize whether _B_ occupies at the instant [beta] the point occupied\nby _A_ at the instant [alpha], I can use a multitude of different\ncriteria. In one my eye intervenes, in another my first finger, in\nanother my second finger, etc. Well, it is sufficient for the criterion\nrelative to one of my fingers to be satisfied in order that all the\nothers should be satisfied, but it is not sufficient that the criterion\nrelative to the eye should be. This is the sense of my assertion. I\ncontent myself with affirming an experimental fact which is ordinarily\nverified.\n\nAt the end of the preceding chapter we analyzed visual space; we saw\nthat to engender this space it is necessary to bring in the retinal\nsensations, the sensation of convergence and the sensation of\naccommodation; that if these last two were not always in accord, visual\nspace would have four dimensions in place of three; we also saw that if\nwe brought in only the retinal sensations, we should obtain 'simple\nvisual space,' of only two dimensions. On the other hand, consider\ntactile space, limiting ourselves to the sensations of a single finger,\nthat is in sum to the assemblage of positions this finger can occupy.\nThis tactile space that we shall analyze in the following section and\nwhich consequently I ask permission not to consider further for the\nmoment, this tactile space, I say, has three dimensions. Why has space\nproperly so called as many dimensions as tactile space and more than\nsimple visual space? It is because touch does not operate at a distance,\nwhile vision does operate at a distance. These two assertions have the\nsame meaning and we have just seen what this is.\n\nNow I return to a point over which I passed rapidly in order not to\ninterrupt the discussion. How do we know that the impressions made on\nour retina by _A_ at the instant [alpha] and _B_ at the instant [beta]\nare transmitted by the same retinal fiber, although these impressions\nare qualitatively different? I have suggested a simple hypothesis, while\nadding that other hypotheses, decidedly more complex, would seem to me\nmore probably true. Here then are these hypotheses, of which I have\nalready said a word. How do we know that the impressions produced by the\nred object A at the instant [alpha], and by the blue object _B_ at the\ninstant [beta], if these two objects have been imaged on the same point\nof the retina, have something in common? The simple hypothesis above\nmade may be rejected and we may suppose that these two impressions,\nqualitatively different, are transmitted by two different though\ncontiguous nervous fibers. What means have I then of knowing that these\nfibers are contiguous? It is probable that we should have none, if the\neye were immovable. It is the movements of the eye which have told us\nthat there is the same relation between the sensation of blue at the\npoint _A_ and the sensation of blue at the point _B_ of the retina as\nbetween the sensation of red at the point _A_ and the sensation of red\nat the point _B_. They have shown us, in fact, that the same movements,\ncorresponding to the same muscular sensations, carry us from the first\nto the second, or from the third to the fourth. I do not emphasize these\nconsiderations, which belong, as one sees, to the question of local\nsigns raised by Lotze.\n\n\n3. _Tactile Space_\n\nThus I know how to recognize the identity of two points, the point\noccupied by _A_ at the instant [alpha] and the point occupied by _B_ at\nthe instant [beta], but only _on one condition_, namely, that I have not\nbudged between the instants [alpha] and [beta]. That does not suffice\nfor our object. Suppose, therefore, that I have moved in any manner in\nthe interval between these two instants, how shall I know whether the\npoint occupied by _A_ at the instant [alpha] is identical with the point\noccupied by _B_ at the instant [beta]? I suppose that at the instant\n[alpha], the object _A_ was in contact with my first finger and that in\nthe same way, at the instant [beta], the object _B_ touches this first\nfinger; but at the same time my muscular sense has told me that in the\ninterval my body has moved. I have considered above two series of\nmuscular sensations _S_ and _S'_, and I have said it sometimes happens\nthat we are led to consider two such series _S_ and _S'_ as inverse one\nof the other, because we have often observed that when these two series\nsucceed one another our primitive impressions are reestablished.\n\nIf then my muscular sense tells me that I have moved between the two\ninstants [alpha] and [beta], but so as to feel successively the two\nseries of muscular sensations _S_ and _S'_ that I consider inverses, I\nshall still conclude, just as if I had not budged, that the points\noccupied by _A_ at the instant [alpha] and by _B_ at the instant [beta]\nare identical, if I ascertain that my first finger touches _A_ at the\ninstant [alpha], and _B_ at the instant [beta].\n\nThis solution is not yet completely satisfactory, as one will see. Let\nus see, in fact, how many dimensions it would make us attribute to\nspace. I wish to compare the two points occupied by _A_ and _B_ at the\ninstants [alpha] and [beta], or (what amounts to the same thing since I\nsuppose that my finger touches _A_ at the instant [alpha] and _B_ at the\ninstant [beta]) I wish to compare the two points occupied by my finger\nat the two instants [alpha] and [beta]. The sole means I use for this\ncomparison is the series [Sigma] of muscular sensations which have\naccompanied the movements of my body between these two instants. The\ndifferent imaginable series [Sigma] form evidently a physical continuum\nof which the number of dimensions is very great. Let us agree, as I have\ndone, not to consider as distinct the two series [Sigma] and [Sigma] +\n_S_ + _S'_, when _S_ and _S'_ are inverses one of the other in the sense\nabove given to this word; in spite of this agreement, the aggregate of\ndistinct series [Sigma] will still form a physical continuum and the\nnumber of dimensions will be less but still very great.\n\nTo each of these series [Sigma] corresponds a point of space; to two\nseries [Sigma] and [Sigma]' thus correspond two points _M_ and _M'_. The\nmeans we have hitherto used enable us to recognize that _M_ and _M'_ are\nnot distinct in two cases: (1) if [Sigma] is identical with [Sigma]';\n(2) if [Sigma]' = [Sigma] + _S_ + _S'_, _S_ and _S'_ being inverses one\nof the other. If in all the other cases we should regard _M_ and _M'_ as\ndistinct, the manifold of points would have as many dimensions as the\naggregate of distinct series [Sigma], that is, much more than three.\n\nFor those who already know geometry, the following explanation would be\neasily comprehensible. Among the imaginable series of muscular\nsensations, there are those which correspond to series of movements\nwhere the finger does not budge. I say that if one does not consider as\ndistinct the series [Sigma] and [Sigma] + [sigma], where the series\n[sigma] corresponds to movements where the finger does not budge, the\naggregate of series will constitute a continuum of three dimensions, but\nthat if one regards as distinct two series [Sigma] and [Sigma]' unless\n[Sigma]' = [Sigma] + _S_ + _S'_, _S_ and _S'_ being inverses, the\naggregate of series will constitute a continuum of more than three\ndimensions.\n\nIn fact, let there be in space a surface _A_, on this surface a line\n_B_, on this line a point _M_. Let C_{0} be the aggregate of all series\n[Sigma]. Let C_{1} be the aggregate of all the series [Sigma], such that\nat the end of corresponding movements the finger is found upon the\nsurface _A_, and C_{2} or C_{3} the aggregate of series [Sigma] such\nthat at the end the finger is found on _B_, or at _M_. It is clear,\nfirst that C_{1} will constitute a cut which will divide C_{0}, that\nC_{2} will be a cut which will divide C_{1}, and C_{3} a cut which will\ndivide C_2. Thence it results, in accordance with our definitions, that\nif C_{3} is a continuum of _n_ dimensions, C_{0} will be a physical\ncontinuum of _n_ + 3 dimensions.\n\nTherefore, let [Sigma] and [Sigma]' = [Sigma] + [sigma] be two series\nforming part of C_{3}; for both, at the end of the movements, the finger\nis found at _M_; thence results that at the beginning and at the end of\nthe series [sigma] the finger is at the same point _M_. This series\n[sigma] is therefore one of those which correspond to movements where\nthe finger does not budge. If [Sigma] and [Sigma] + [sigma] are not\nregarded as distinct, all the series of C_{3} blend into one; therefore\nC_{3} will have 0 dimension, and C_{0} will have 3, as I wished to\nprove. If, on the contrary, I do not regard [Sigma] and [Sigma] +\n[sigma] as blending (unless [sigma] = _S_ + _S'_, _S_ and _S'_ being\ninverses), it is clear that C_{3} will contain a great number of series\nof distinct sensations; because, without the finger budging, the body\nmay take a multitude of different attitudes. Then C_{3} will form a\ncontinuum and C_{0} will have more than three dimensions, and this also\nI wished to prove.\n\nWe who do not yet know geometry can not reason in this way; we can only\nverify. But then a question arises; how, before knowing geometry, have\nwe been led to distinguish from the others these series [sigma] where\nthe finger does not budge? It is, in fact, only after having made this\ndistinction that we could be led to regard [Sigma] and [Sigma] + [sigma]\nas identical, and it is on this condition alone, as we have just seen,\nthat we can arrive at space of three dimensions.\n\nWe are led to distinguish the series [sigma], because it often happens\nthat when we have executed the movements which correspond to these\nseries [sigma] of muscular sensations, the tactile sensations which are\ntransmitted to us by the nerve of the finger that we have called the\nfirst finger, persist and are not altered by these movements. Experience\nalone tells us that and it alone could tell us.\n\nIf we have distinguished the series of muscular sensations _S_ + _S'_\nformed by the union of two inverse series, it is because they preserve\nthe totality of our impressions; if now we distinguish the series\n[sigma], it is because they preserve _certain_ of our impressions. (When\nI say that a series of muscular sensations _S_ 'preserves' one of our\nimpressions _A_, I mean that we ascertain that if we feel the impression\n_A_, then the muscular sensations _S_, we _still_ feel the impression\n_A_ _after_ these sensations _S_.)\n\nI have said above it often happens that the series [sigma] do not alter\nthe tactile impressions felt by our first finger; I said _often_, I did\nnot say _always_. This it is that we express in our ordinary language by\nsaying that the tactile impressions would not be altered if the finger\nhas not moved, _on the condition_ that _neither has_ the object _A_,\nwhich was in contact with this finger, moved. Before knowing geometry,\nwe could not give this explanation; all we could do is to ascertain that\nthe impression often persists, but not always.\n\nBut that the impression often continues is enough to make the series\n[sigma] appear remarkable to us, to lead us to put in the same class the\nseries [Sigma] and [Sigma] + [sigma], and hence not regard them as\ndistinct. Under these conditions we have seen that they will engender a\nphysical continuum of three dimensions.\n\nBehold then a space of three dimensions engendered by my first finger.\nEach of my fingers will create one like it. It remains to consider how\nwe are led to regard them as identical with visual space, as identical\nwith geometric space.\n\nBut one reflection before going further; according to the foregoing, we\nknow the points of space, or more generally the final situation of our\nbody, only by the series of muscular sensations revealing to us the\nmovements which have carried us from a certain initial situation to this\nfinal situation. But it is clear that this final situation will depend,\non the one hand, upon these movements and, _on the other hand, upon the\ninitial situation_ from which we set out. Now these movements are\nrevealed to us by our muscular sensations; but nothing tells us the\ninitial situation; nothing can distinguish it for us from all the other\npossible situations. This puts well in evidence the essential relativity\nof space.\n\n\n4. _Identity of the Different Spaces_\n\nWe are therefore led to compare the two continua _C_ and _C'_\nengendered, for instance, one by my first finger _D_, the other by my\nsecond finger _D'_. These two physical continua both have three\ndimensions. To each element of the continuum _C_, or, if you prefer, to\neach point of the first tactile space, corresponds a series of muscular\nsensations [Sigma], which carry me from a certain initial situation to a\ncertain final situation.[8] Moreover, the same point of this first space\nwill correspond to [Sigma] and [Sigma] + [sigma], if [sigma] is a series\nof which we know that it does not make the finger _D_ move.\n\n [8] In place of saying that we refer space to axes rigidly bound to\n our body, perhaps it would be better to say, in conformity to\n what precedes, that we refer it to axes rigidly bound to the\n initial situation of our body.\n\nSimilarly to each element of the continuum _C'_, or to each point of the\nsecond tactile space, corresponds a series of sensations [Sigma]', and\nthe same point will correspond to [Sigma]' and to [Sigma]' + [sigma]',\nif [sigma]' is a series which does not make the finger _D'_ move.\n\nWhat makes us distinguish the various series designated [sigma] from\nthose called [sigma]' is that the first do not alter the tactile\nimpressions felt by the finger _D_ and the second preserve those the\nfinger _D'_ feels.\n\nNow see what we ascertain: in the beginning my finger _D'_ feels a\nsensation _A'_; I make movements which produce muscular sensations _S_;\nmy finger _D_ feels the impression _A_; I make movements which produce a\nseries of sensations [sigma]; my finger _D_ continues to feel the\nimpression _A_, since this is the characteristic property of the series\n[sigma]; I then make movements which produce the series _S'_ of muscular\nsensations, _inverse_ to _S_ in the sense above given to this word. I\nascertain then that my finger _D'_ feels anew the impression _A'_. (It\nis of course understood that _S_ has been suitably chosen.)\n\nThis means that the series _S_ + [sigma] + _S'_, preserving the tactile\nimpressions of the finger _D'_, is one of the series I have called\n[sigma]'. Inversely, if one takes any series [sigma]', _S'_ + [sigma]' +\n_S_ will be one of the series that we call [sigma]'.\n\nThus if _S_ is suitably chosen, _S_ + [sigma] + _S'_ will be a series\n[sigma]', and by making [sigma] vary in all possible ways, we shall\nobtain all the possible series [sigma]'.\n\nNot yet knowing geometry, we limit ourselves to verifying all that, but\nhere is how those who know geometry would explain the fact. In the\nbeginning my finger _D'_ is at the point _M_, in contact with the object\n_a_, which makes it feel the impression _A'_. I make the movements\ncorresponding to the series _S_; I have said that this series should be\nsuitably chosen, I should so make this choice that these movements carry\nthe finger _D_ to the point originally occupied by the finger _D'_, that\nis, to the point _M_; this finger _D_ will thus be in contact with the\nobject _a_, which will make it feel the impression _A_.\n\nI then make the movements corresponding to the series [sigma]; in these\nmovements, by hypothesis, the position of the finger _D_ does not\nchange, this finger therefore remains in contact with the object a and\ncontinues to feel the impression _A_. Finally I make the movements\ncorresponding to the series _S'_. As _S'_ is inverse to _S_, these\nmovements carry the finger _D'_ to the point previously occupied by the\nfinger _D_, that is, to the point _M_. If, as may be supposed, the\nobject _a_ has not budged, this finger _D'_ will be in contact with this\nobject and will feel anew the impression _A'_.... _Q.E.D._\n\nLet us see the consequences. I consider a series of muscular sensations\n[Sigma]. To this series will correspond a point _M_ of the first tactile\nspace. Now take again the two series _S_ and _S'_, inverses of one\nanother, of which we have just spoken. To the series _S_ + [Sigma] +\n_S'_ will correspond a point _N_ of the second tactile space, since to\nany series of muscular sensations corresponds, as we have said, a\npoint, whether in the first space or in the second.\n\nI am going to consider the two points _N_ and _M_, thus defined, as\ncorresponding. What authorizes me so to do? For this correspondence to\nbe admissible, it is necessary that if two points _M_ and _M'_,\ncorresponding in the first space to two series [Sigma] and [Sigma]', are\nidentical, so also are the two corresponding points of the second space\n_N_ and _N'_, that is, the two points which correspond to the two series\n_S_ + [Sigma] + _S'_ and _S_ + [Sigma]' + _S'_. Now we shall see that\nthis condition is fulfilled.\n\nFirst a remark. As _S_ and _S'_ are inverses of one another, we shall\nhave _S_ + _S'_ = 0, and consequently _S_ + _S'_ + [Sigma] = [Sigma] +\n_S_ + _S'_ = [Sigma], or again [Sigma] + _S_ + _S'_ + [Sigma]' = [Sigma]\n+ [Sigma]'; but it does not follow that we have _S_ + [Sigma] + _S'_ =\n[Sigma]; because, though we have used the addition sign to represent the\nsuccession of our sensations, it is clear that the order of this\nsuccession is not indifferent: we can not, therefore, as in ordinary\naddition, invert the order of the terms; to use abridged language, our\noperations are associative, but not commutative.\n\nThat fixed, in order that [Sigma] and [Sigma]' should correspond to the\nsame point _M_ = _M'_ of the first space, it is necessary and sufficient\nfor us to have [Sigma]' = [Sigma] + [sigma]. We shall then have: _S_ +\n[Sigma]' + _S'_ = _S_ + [Sigma] + [sigma] + _S'_ = _S_ + [Sigma] + _S'_\n+ _S_ + [sigma] + _S'_.\n\nBut we have just ascertained that _S_ + [sigma] + _S'_ was one of the\nseries [sigma]'. We shall therefore have: _S_ + [Sigma]' + _S'_ = _S_ +\n[Sigma] + _S'_ + [sigma]', which means that the series _S_ + [Sigma]' +\n_S'_ and _S_ + [Sigma] + _S'_ correspond to the same point _N_ = _N'_ of\nthe second space. Q.E.D.\n\nOur two spaces therefore correspond point for point; they can be\n'transformed' one into the other; they are isomorphic. How are we led to\nconclude thence that they are identical?\n\nConsider the two series [sigma] and _S_ + [sigma] + _S'_ = [sigma]'. I\nhave said that often, but not always, the series [sigma] preserves the\ntactile impression _A_ felt by the finger _D_; and similarly it often\nhappens, but not always, that the series [sigma]' preserves the tactile\nimpression _A'_ felt by the finger _D'_. Now I ascertain that it happens\n_very often_ (that is, much more often than what I have just called\n'often') that when the series [sigma] has preserved the impression _A_\nof the finger _D_, the series [sigma]' preserves at the same time the\nimpression _A'_ of the finger _D'_; and, inversely, that if the first\nimpression is altered, the second is likewise. That happens _very\noften_, but not always.\n\nWe interpret this experimental fact by saying that the unknown object\n_a_ which gives the impression _A_ to the finger _D_ is identical with\nthe unknown object _a'_ which gives the impression _A'_ to the finger\n_D'_. And in fact when the first object moves, which the disappearance\nof the impression _A_ tells us, the second likewise moves, since the\nimpression _A'_ disappears likewise. When the first object remains\nmotionless, the second remains motionless. If these two objects are\nidentical, as the first is at the point _M_ of the first space and the\nsecond at the point _N_ of the second space, these two points are\nidentical. This is how we are led to regard these two spaces as\nidentical; or better, this is what we mean when we say that they are\nidentical.\n\nWhat we have just said of the identity of the two tactile spaces makes\nunnecessary our discussing the question of the identity of tactile space\nand visual space, which could be treated in the same way.\n\n\n5. _Space and Empiricism_\n\nIt seems that I am about to be led to conclusions in conformity with\nempiristic ideas. I have, in fact, sought to put in evidence the r\u00f4le of\nexperience and to analyze the experimental facts which intervene in the\ngenesis of space of three dimensions. But whatever may be the importance\nof these facts, there is one thing we must not forget and to which\nbesides I have more than once called attention. These experimental facts\nare often verified but not always. That evidently does not mean that\nspace has often three dimensions, but not always.\n\nI know well that it is easy to save oneself and that, if the facts do\nnot verify, it will be easily explained by saying that the exterior\nobjects have moved. If experience succeeds, we say that it teaches us\nabout space; if it does not succeed, we hie to exterior objects which we\naccuse of having moved; in other words, if it does not succeed, it is\ngiven a fillip.\n\nThese fillips are legitimate; I do not refuse to admit them; but they\nsuffice to tell us that the properties of space are not experimental\ntruths, properly so called. If we had wished to verify other laws, we\ncould have succeeded also, by giving other analogous fillips. Should we\nnot always have been able to justify these fillips by the same reasons?\nOne could at most have said to us: 'Your fillips are doubtless\nlegitimate, but you abuse them; why move the exterior objects so often?'\n\nTo sum up, experience does not prove to us that space has three\ndimensions; it only proves to us that it is convenient to attribute\nthree to it, because thus the number of fillips is reduced to a minimum.\n\nI will add that experience brings us into contact only with\nrepresentative space, which is a physical continuum, never with\ngeometric space, which is a mathematical continuum. At the very most it\nwould appear to tell us that it is convenient to give to geometric space\nthree dimensions, so that it may have as many as representative space.\n\nThe empiric question may be put under another form. Is it impossible to\nconceive physical phenomena, the mechanical phenomena, for example,\notherwise than in space of three dimensions? We should thus have an\nobjective experimental proof, so to speak, independent of our\nphysiology, of our modes of representation.\n\nBut it is not so; I shall not here discuss the question completely, I\nshall confine myself to recalling the striking example given us by the\nmechanics of Hertz. You know that the great physicist did not believe in\nthe existence of forces, properly so called; he supposed that visible\nmaterial points are subjected to certain invisible bonds which join them\nto other invisible points and that it is the effect of these invisible\nbonds that we attribute to forces.\n\nBut that is only a part of his ideas. Suppose a system formed of n\nmaterial points, visible or not; that will give in all 3_n_ coordinates;\nlet us regard them as the coordinates of a _single_ point in space of\n3_n_ dimensions. This single point would be constrained to remain upon a\nsurface (of any number of dimensions < 3_n_) in virtue of the bonds of\nwhich we have just spoken; to go on this surface from one point to\nanother, it would always take the shortest way; this would be the\nsingle principle which would sum up all mechanics.\n\nWhatever should be thought of this hypothesis, whether we be allured by\nits simplicity, or repelled by its artificial character, the simple fact\nthat Hertz was able to conceive it, and to regard it as more convenient\nthan our habitual hypotheses, suffices to prove that our ordinary ideas,\nand, in particular, the three dimensions of space, are in no wise\nimposed upon mechanics with an invincible force.\n\n\n6. _Mind and Space_\n\nExperience, therefore, has played only a single r\u00f4le, it has served as\noccasion. But this r\u00f4le was none the less very important; and I have\nthought it necessary to give it prominence. This r\u00f4le would have been\nuseless if there existed an _a priori_ form imposing itself upon our\nsensitivity, and which was space of three dimensions.\n\nDoes this form exist, or, if you choose, can we represent to ourselves\nspace of more than three dimensions? And first what does this question\nmean? In the true sense of the word, it is clear that we can not\nrepresent to ourselves space of four, nor space of three, dimensions; we\ncan not first represent them to ourselves empty, and no more can we\nrepresent to ourselves an object either in space of four, or in space of\nthree, dimensions: (1) Because these spaces are both infinite and we can\nnot represent to ourselves a figure _in_ space, that is, the part _in_\nthe whole, without representing the whole, and that is impossible,\nbecause it is infinite; (2) because these spaces are both mathematical\ncontinua, and we can represent to ourselves only the physical continuum;\n(3) because these spaces are both homogeneous, and the frames in which\nwe enclose our sensations, being limited, can not be homogeneous.\n\nThus the question put can only be understood in one way; is it possible\nto imagine that, the results of the experiences related above having\nbeen different, we might have been led to attribute to space more than\nthree dimensions; to imagine, for instance, that the sensation of\naccommodation might not be constantly in accord with the sensation of\nconvergence of the eyes; or indeed that the experiences of which we\nhave spoken in \u00a7 2, and of which we express the result by saying 'that\ntouch does not operate at a distance,' might have led us to an inverse\nconclusion.\n\nAnd then yes evidently that is possible; from the moment one imagines an\nexperience, one imagines just thereby the two contrary results it may\ngive. That is possible, but that is difficult, because we have to\novercome a multitude of associations of ideas, which are the fruit of a\nlong personal experience and of the still longer experience of the race.\nIs it these associations (or at least those of them that we have\ninherited from our ancestors), which constitute this _a priori_ form of\nwhich it is said that we have pure intuition? Then I do not see why one\nshould declare it refractory to analysis and should deny me the right of\ninvestigating its origin.\n\nWhen it is said that our sensations are 'extended' only one thing can be\nmeant, that is that they are always associated with the idea of certain\nmuscular sensations, corresponding to the movements which enable us to\nreach the object which causes them, which enable us, in other words, to\ndefend ourselves against it. And it is just because this association is\nuseful for the defense of the organism, that it is so old in the history\nof the species and that it seems to us indestructible. Nevertheless, it\nis only an association and we can conceive that it may be broken; so\nthat we may not say that sensation can not enter consciousness without\nentering in space, but that in fact it does not enter consciousness\nwithout entering in space, which means, without being entangled in this\nassociation.\n\nNo more can I understand one's saying that the idea of time is logically\nsubsequent to space, since we can represent it to ourselves only under\nthe form of a straight line; as well say that time is logically\nsubsequent to the cultivation of the prairies, since it is usually\nrepresented armed with a scythe. That one can not represent to himself\nsimultaneously the different parts of time, goes without saying, since\nthe essential character of these parts is precisely not to be\nsimultaneous. That does not mean that we have not the intuition of time.\nSo far as that goes, no more should we have that of space, because\nneither can we represent it, in the proper sense of the word, for the\nreasons I have mentioned. What we represent to ourselves under the name\nof straight is a crude image which as ill resembles the geometric\nstraight as it does time itself.\n\nWhy has it been said that every attempt to give a fourth dimension to\nspace always carries this one back to one of the other three? It is easy\nto understand. Consider our muscular sensations and the 'series' they\nmay form. In consequence of numerous experiences, the ideas of these\nseries are associated together in a very complex woof, our series are\n_classed_. Allow me, for convenience of language, to express my thought\nin a way altogether crude and even inexact by saying that our series of\nmuscular sensations are classed in three classes corresponding to the\nthree dimensions of space. Of course this classification is much more\ncomplicated than that, but that will suffice to make my reasoning\nunderstood. If I wish to imagine a fourth dimension, I shall suppose\nanother series of muscular sensations, making part of a fourth class.\nBut as _all_ my muscular sensations have already been classed in one of\nthe three pre-existent classes, I can only represent to myself a series\nbelonging to one of these three classes, so that my fourth dimension is\ncarried back to one of the other three.\n\nWhat does that prove? This: that it would have been necessary first to\ndestroy the old classification and replace it by a new one in which the\nseries of muscular sensations should have been distributed into four\nclasses. The difficulty would have disappeared.\n\nIt is presented sometimes under a more striking form. Suppose I am\nenclosed in a chamber between the six impassable boundaries formed by\nthe four walls, the floor and the ceiling; it will be impossible for me\nto get out and to imagine my getting out. Pardon, can you not imagine\nthat the door opens, or that two of these walls separate? But of course,\nyou answer, one must suppose that these walls remain immovable. Yes, but\nit is evident that I have the right to move; and then the walls that we\nsuppose absolutely at rest will be in motion with regard to me. Yes, but\nsuch a relative motion can not be arbitrary; when objects are at rest,\ntheir relative motion with regard to any axes is that of a rigid solid;\nnow, the apparent motions that you imagine are not in conformity with\nthe laws of motion of a rigid solid. Yes, but it is experience which has\ntaught us the laws of motion of a rigid solid; nothing would prevent our\n_imagining_ them different. To sum up, for me to imagine that I get out\nof my prison, I have only to imagine that the walls seem to open, when I\nmove.\n\nI believe, therefore, that if by space is understood a mathematical\ncontinuum of three dimensions, were it otherwise amorphous, it is the\nmind which constructs it, but it does not construct it out of nothing;\nit needs materials and models. These materials, like these models,\npreexist within it. But there is not a single model which is imposed\nupon it; it has _choice_; it may choose, for instance, between space of\nfour and space of three dimensions. What then is the r\u00f4le of experience?\nIt gives the indications following which the choice is made.\n\nAnother thing: whence does space get its quantitative character? It\ncomes from the r\u00f4le which the series of muscular sensations play in its\ngenesis. These are series which may _repeat themselves_, and it is from\ntheir repetition that number comes; it is because they can repeat\nthemselves indefinitely that space is infinite. And finally we have\nseen, at the end of section 3, that it is also because of this that\nspace is relative. So it is repetition which has given to space its\nessential characteristics; now, repetition supposes time; this is enough\nto tell that time is logically anterior to space.\n\n7. _R\u00f4le of the Semicircular Canals_\n\nI have not hitherto spoken of the r\u00f4le of certain organs to which the\nphysiologists attribute with reason a capital importance, I mean the\nsemicircular canals. Numerous experiments have sufficiently shown that\nthese canals are necessary to our sense of orientation; but the\nphysiologists are not entirely in accord; two opposing theories have\nbeen proposed, that of Mach-Delage and that of M. de Cyon.\n\nM. de Cyon is a physiologist who has made his name illustrious by\nimportant discoveries on the innervation of the heart; I can not,\nhowever, agree with his ideas on the question before us. Not being a\nphysiologist, I hesitate to criticize the experiments he has directed\nagainst the adverse theory of Mach-Delage; it seems to me, however, that\nthey are not convincing, because in many of them the _total_ pressure\nwas made to vary in one of the canals, while, physiologically, what\nvaries is the _difference_ between the pressures on the two extremities\nof the canal; in others the organs were subjected to profound lesions,\nwhich must alter their functions.\n\nBesides, this is not important; the experiments, if they were\nirreproachable, might be convincing against the old theory. They would\nnot be convincing _for_ the new theory. In fact, if I have rightly\nunderstood the theory, my explaining it will be enough for one to\nunderstand that it is impossible to conceive of an experiment confirming\nit.\n\nThe three pairs of canals would have as sole function to tell us that\nspace has three dimensions. Japanese mice have only two pairs of canals;\nthey believe, it would seem, that space has only two dimensions, and\nthey manifest this opinion in the strangest way; they put themselves in\na circle, and, so ordered, they spin rapidly around. The lampreys,\nhaving only one pair of canals, believe that space has only one\ndimension, but their manifestations are less turbulent.\n\nIt is evident that such a theory is inadmissible. The sense-organs are\ndesigned to tell us of _changes_ which happen in the exterior world. We\ncould not understand why the Creator should have given us organs\ndestined to cry without cease: Remember that space has three dimensions,\nsince the number of these three dimensions is not subject to change.\n\nWe must, therefore, come back to the theory of Mach-Delage. What the\nnerves of the canals can tell us is the difference of pressure on the\ntwo extremities of the same canal, and thereby: (1) the direction of the\nvertical with regard to three axes rigidly bound to the head; (2) the\nthree components of the acceleration of translation of the center of\ngravity of the head; (3) the centrifugal forces developed by the\nrotation of the head; (4) the acceleration of the motion of rotation of\nthe head.\n\nIt follows from the experiments of M. Delage that it is this last\nindication which is much the most important; doubtless because the\nnerves are less sensible to the difference of pressure itself than to\nthe brusque variations of this difference. The first three indications\nmay thus be neglected.\n\nKnowing the acceleration of the motion of rotation of the head at each\ninstant, we deduce from it, by an unconscious integration, the final\norientation of the head, referred to a certain initial orientation taken\nas origin. The circular canals contribute, therefore, to inform us of\nthe movements that we have executed, and that on the same ground as the\nmuscular sensations. When, therefore, above we speak of the series _S_\nor of the series [Sigma], we should say, not that these were series of\nmuscular sensations alone, but that they were series at the same time of\nmuscular sensations and of sensations due to the semicircular canals.\nApart from this addition, we should have nothing to change in what\nprecedes.\n\nIn the series _S_ and [Sigma], these sensations of the semicircular\ncanals evidently hold a very important place. Yet alone they would not\nsuffice, because they can tell us only of the movements of the head;\nthey tell us nothing of the relative movements of the body or of the\nmembers in regard to the head. And more, it seems that they tell us only\nof the rotations of the head and not of the translations it may\nundergo.\n\n\n\n\nPART II\n\n\nTHE PHYSICAL SCIENCES\n\n\n\n\nCHAPTER V\n\nANALYSIS AND PHYSICS\n\n\nI\n\nYou have doubtless often been asked of what good is mathematics and\nwhether these delicate constructions entirely mind-made are not\nartificial and born of our caprice.\n\nAmong those who put this question I should make a distinction; practical\npeople ask of us only the means of money-making. These merit no reply;\nrather would it be proper to ask of them what is the good of\naccumulating so much wealth and whether, to get time to acquire it, we\nare to neglect art and science, which alone give us souls capable of\nenjoying it, 'and for life's sake to sacrifice all reasons for living.'\n\nBesides, a science made solely in view of applications is impossible;\ntruths are fecund only if bound together. If we devote ourselves solely\nto those truths whence we expect an immediate result, the intermediary\nlinks are wanting and there will no longer be a chain.\n\nThe men most disdainful of theory get from it, without suspecting it,\ntheir daily bread; deprived of this food, progress would quickly cease,\nand we should soon congeal into the immobility of old China.\n\nBut enough of uncompromising practicians! Besides these, there are those\nwho are only interested in nature and who ask us if we can enable them\nto know it better.\n\nTo answer these, we have only to show them the two monuments already\nrough-hewn, Celestial Mechanics and Mathematical Physics.\n\nThey would doubtless concede that these structures are well worth the\ntrouble they have cost us. But this is not enough. Mathematics has a\ntriple aim. It must furnish an instrument for the study of nature. But\nthat is not all: it has a philosophic aim and, I dare maintain, an\nesthetic aim. It must aid the philosopher to fathom the notions of\nnumber, of space, of time. And above all, its adepts find therein\ndelights analogous to those given by painting and music. They admire the\ndelicate harmony of numbers and forms; they marvel when a new discovery\nopens to them an unexpected perspective; and has not the joy they thus\nfeel the esthetic character, even though the senses take no part\ntherein? Only a privileged few are called to enjoy it fully, it is true,\nbut is not this the case for all the noblest arts?\n\nThis is why I do not hesitate to say that mathematics deserves to be\ncultivated for its own sake, and the theories inapplicable to physics as\nwell as the others. Even if the physical aim and the esthetic aim were\nnot united, we ought not to sacrifice either.\n\nBut more: these two aims are inseparable and the best means of attaining\none is to aim at the other, or at least never to lose sight of it. This\nis what I am about to try to demonstrate in setting forth the nature of\nthe relations between the pure science and its applications.\n\nThe mathematician should not be for the physicist a mere purveyor of\nformulas; there should be between them a more intimate collaboration.\nMathematical physics and pure analysis are not merely adjacent powers,\nmaintaining good neighborly relations; they mutually interpenetrate and\ntheir spirit is the same. This will be better understood when I have\nshown what physics gets from mathematics and what mathematics, in\nreturn, borrows from physics.\n\n\nII\n\nThe physicist can not ask of the analyst to reveal to him a new truth;\nthe latter could at most only aid him to foresee it. It is a long time\nsince one still dreamt of forestalling experiment, or of constructing\nthe entire world on certain premature hypotheses. Since all those\nconstructions in which one yet took a na\u00efve delight it is an age, to-day\nonly their ruins remain.\n\nAll laws are therefore deduced from experiment; but to enunciate them, a\nspecial language is needful; ordinary language is too poor, it is\nbesides too vague, to express relations so delicate, so rich, and so\nprecise.\n\nThis therefore is one reason why the physicist can not do without\nmathematics; it furnishes him the only language he can speak. And a\nwell-made language is no indifferent thing; not to go beyond physics,\nthe unknown man who invented the word _heat_ devoted many generations to\nerror. Heat has been treated as a substance, simply because it was\ndesignated by a substantive, and it has been thought indestructible.\n\nOn the other hand, he who invented the word _electricity_ had the\nunmerited good fortune to implicitly endow physics with a _new_ law,\nthat of the conservation of electricity, which, by a pure chance, has\nbeen found exact, at least until now.\n\nWell, to continue the simile, the writers who embellish a language, who\ntreat it as an object of art, make of it at the same time a more supple\ninstrument, more apt for rendering shades of thought.\n\nWe understand, then, how the analyst, who pursues a purely esthetic aim,\nhelps create, just by that, a language more fit to satisfy the\nphysicist.\n\nBut this is not all: law springs from experiment, but not immediately.\nExperiment is individual, the law deduced from it is general; experiment\nis only approximate, the law is precise, or at least pretends to be.\nExperiment is made under conditions always complex, the enunciation of\nthe law eliminates these complications. This is what is called\n'correcting the systematic errors.'\n\nIn a word, to get the law from experiment, it is necessary to\ngeneralize; this is a necessity imposed upon the most circumspect\nobserver. But how generalize? Every particular truth may evidently be\nextended in an infinity of ways. Among these thousand routes opening\nbefore us, it is necessary to make a choice, at least provisional; in\nthis choice, what shall guide us?\n\nIt can only be analogy. But how vague is this word! Primitive man knew\nonly crude analogies, those which strike the senses, those of colors or\nof sounds. He never would have dreamt of likening light to radiant\nheat.\n\nWhat has taught us to know the true, profound analogies, those the eyes\ndo not see but reason divines?\n\nIt is the mathematical spirit, which disdains matter to cling only to\npure form. This it is which has taught us to give the same name to\nthings differing only in material, to call by the same name, for\ninstance, the multiplication of quaternions and that of whole numbers.\n\nIf quaternions, of which I have just spoken, had not been so promptly\nutilized by the English physicists, many persons would doubtless see in\nthem only a useless fancy, and yet, in teaching us to liken what\nappearances separate, they would have already rendered us more apt to\npenetrate the secrets of nature.\n\nSuch are the services the physicist should expect of analysis; but for\nthis science to be able to render them, it must be cultivated in the\nbroadest fashion without immediate expectation of utility--the\nmathematician must have worked as artist.\n\nWhat we ask of him is to help us to see, to discern our way in the\nlabyrinth which opens before us. Now, he sees best who stands highest.\nExamples abound, and I limit myself to the most striking.\n\nThe first will show us how to change the language suffices to reveal\ngeneralizations not before suspected.\n\nWhen Newton's law has been substituted for Kepler's we still know only\nelliptic motion. Now, in so far as concerns this motion, the two laws\ndiffer only in form; we pass from one to the other by a simple\ndifferentiation. And yet from Newton's law may be deduced by an\nimmediate generalization all the effects of perturbations and the whole\nof celestial mechanics. If, on the other hand, Kepler's enunciation had\nbeen retained, no one would ever have regarded the orbits of the\nperturbed planets, those complicated curves of which no one has ever\nwritten the equation, as the natural generalizations of the ellipse. The\nprogress of observations would only have served to create belief in\nchaos.\n\nThe second example is equally deserving of consideration.\n\nWhen Maxwell began his work, the laws of electro-dynamics admitted up to\nhis time accounted for all the known facts. It was not a new experiment\nwhich came to invalidate them. But in looking at them under a new bias,\nMaxwell saw that the equations became more symmetrical when a term was\nadded, and besides, this term was too small to produce effects\nappreciable with the old methods.\n\nYou know that Maxwell's _a priori_ views awaited for twenty years an\nexperimental confirmation; or, if you prefer, Maxwell was twenty years\nahead of experiment. How was this triumph obtained?\n\nIt was because Maxwell was profoundly steeped in the sense of\nmathematical symmetry; would he have been so, if others before him had\nnot studied this symmetry for its own beauty?\n\nIt was because Maxwell was accustomed to 'think in vectors,' and yet it\nwas through the theory of imaginaries (neomonics) that vectors were\nintroduced into analysis. And those who invented imaginaries hardly\nsuspected the advantage which would be obtained from them for the study\nof the real world, of this the name given them is proof sufficient.\n\nIn a word, Maxwell was perhaps not an able analyst, but this ability\nwould have been for him only a useless and bothersome baggage. On the\nother hand, he had in the highest degree the intimate sense of\nmathematical analogies. Therefore it is that he made good mathematical\nphysics.\n\nMaxwell's example teaches us still another thing.\n\nHow should the equations of mathematical physics be treated? Should we\nsimply deduce all the consequences and regard them as intangible\nrealities? Far from it; what they should teach us above all is what can\nand what should be changed. It is thus that we get from them something\nuseful.\n\nThe third example goes to show us how we may perceive mathematical\nanalogies between phenomena which have physically no relation either\napparent or real, so that the laws of one of these phenomena aid us to\ndivine those of the other.\n\nThe very same equation, that of Laplace, is met in the theory of\nNewtonian attraction, in that of the motion of liquids, in that of the\nelectric potential, in that of magnetism, in that of the propagation of\nheat and in still many others. What is the result? These theories seem\nimages copied one from the other; they are mutually illuminating,\nborrowing their language from each other; ask electricians if they do\nnot felicitate themselves on having invented the phrase flow of force,\nsuggested by hydrodynamics and the theory of heat.\n\nThus mathematical analogies not only may make us foresee physical\nanalogies, but besides do not cease to be useful when these latter fail.\n\nTo sum up, the aim of mathematical physics is not only to facilitate for\nthe physicist the numerical calculation of certain constants or the\nintegration of certain differential equations. It is besides, it is\nabove all, to reveal to him the hidden harmony of things in making him\nsee them in a new way.\n\nOf all the parts of analysis, the most elevated, the purest, so to\nspeak, will be the most fruitful in the hands of those who know how to\nuse them.\n\n\nIII\n\nLet us now see what analysis owes to physics.\n\nIt would be necessary to have completely forgotten the history of\nscience not to remember that the desire to understand nature has had on\nthe development of mathematics the most constant and happiest influence.\n\nIn the first place the physicist sets us problems whose solution he\nexpects of us. But in proposing them to us, he has largely paid us in\nadvance for the service we shall render him, if we solve them.\n\nIf I may be allowed to continue my comparison with the fine arts, the\npure mathematician who should forget the existence of the exterior world\nwould be like a painter who knew how to harmoniously combine colors and\nforms, but who lacked models. His creative power would soon be\nexhausted.\n\nThe combinations which numbers and symbols may form are an infinite\nmultitude. In this multitude how shall we choose those which are worthy\nto fix our attention? Shall we let ourselves be guided solely by our\ncaprice? This caprice, which itself would besides soon tire, would\ndoubtless carry us very far apart and we should quickly cease to\nunderstand each other.\n\nBut this is only the smaller side of the question. Physics will\ndoubtless prevent our straying, but it will also preserve us from a\ndanger much more formidable; it will prevent our ceaselessly going\naround in the same circle.\n\nHistory proves that physics has not only forced us to choose among\nproblems which came in a crowd; it has imposed upon us such as we should\nwithout it never have dreamed of. However varied may be the imagination\nof man, nature is still a thousand times richer. To follow her we must\ntake ways we have neglected, and these paths lead us often to summits\nwhence we discover new countries. What could be more useful!\n\nIt is with mathematical symbols as with physical realities; it is in\ncomparing the different aspects of things that we are able to comprehend\ntheir inner harmony, which alone is beautiful and consequently worthy of\nour efforts.\n\nThe first example I shall cite is so old we are tempted to forget it; it\nis nevertheless the most important of all.\n\nThe sole natural object of mathematical thought is the whole number. It\nis the external world which has imposed the continuum upon us, which we\ndoubtless have invented, but which it has forced us to invent. Without\nit there would be no infinitesimal analysis; all mathematical science\nwould reduce itself to arithmetic or to the theory of substitutions.\n\nOn the contrary, we have devoted to the study of the continuum almost\nall our time and all our strength. Who will regret it; who will think\nthat this time and this strength have been wasted? Analysis unfolds\nbefore us infinite perspectives that arithmetic never suspects; it shows\nus at a glance a majestic assemblage whose array is simple and\nsymmetric; on the contrary, in the theory of numbers, where reigns the\nunforeseen, the view is, so to speak, arrested at every step.\n\nDoubtless it will be said that outside of the whole number there is no\nrigor, and consequently no mathematical truth; that the whole number\nhides everywhere, and that we must strive to render transparent the\nscreens which cloak it, even if to do so we must resign ourselves to\ninterminable repetitions. Let us not be such purists and let us be\ngrateful to the continuum, which, if _all_ springs from the whole\nnumber, was alone capable of making _so much_ proceed therefrom.\n\nNeed I also recall that M. Hermite obtained a surprising advantage from\nthe introduction of continuous variables into the theory of numbers?\nThus the whole number's own domain is itself invaded, and this invasion\nhas established order where disorder reigned.\n\nSee what we owe to the continuum and consequently to physical nature.\n\nFourier's series is a precious instrument of which analysis makes\ncontinual use, it is by this means that it has been able to represent\ndiscontinuous functions; Fourier invented it to solve a problem of\nphysics relative to the propagation of heat. If this problem had not\ncome up naturally, we should never have dared to give discontinuity its\nrights; we should still long have regarded continuous functions as the\nonly true functions.\n\nThe notion of function has been thereby considerably extended and has\nreceived from some logician-analysts an unforeseen development. These\nanalysts have thus adventured into regions where reigns the purest\nabstraction and have gone as far away as possible from the real world.\nYet it is a problem of physics which has furnished them the occasion.\n\nAfter Fourier's series, other analogous series have entered the domain\nof analysis; they have entered by the same door; they have been imagined\nin view of applications.\n\nThe theory of partial differential equations of the second order has an\nanalogous history. It has been developed chiefly by and for physics. But\nit may take many forms, because such an equation does not suffice to\ndetermine the unknown function, it is necessary to adjoin to it\ncomplementary conditions which are called conditions at the limits;\nwhence many different problems.\n\nIf the analysts had abandoned themselves to their natural tendencies,\nthey would never have known but one, that which Madame Kovalevski has\ntreated in her celebrated memoir. But there are a multitude of others\nwhich they would have ignored. Each of the theories of physics, that of\nelectricity, that of heat, presents us these equations under a new\naspect. It may, therefore, be said that without these theories we should\nnot know partial differential equations.\n\nIt is needless to multiply examples. I have given enough to be able to\nconclude: when physicists ask of us the solution of a problem, it is not\na duty-service they impose upon us, it is on the contrary we who owe\nthem thanks.\n\n\nIV\n\nBut this is not all; physics not only gives us the occasion to solve\nproblems; it aids us to find the means thereto, and that in two ways. It\nmakes us foresee the solution; it suggests arguments to us.\n\nI have spoken above of Laplace's equation which is met in a multitude of\ndiverse physical theories. It is found again in geometry, in the theory\nof conformal representation and in pure analysis, in that of\nimaginaries.\n\nIn this way, in the study of functions of complex variables, the\nanalyst, alongside of the geometric image, which is his usual\ninstrument, finds many physical images which he may make use of with the\nsame success. Thanks to these images, he can see at a glance what pure\ndeduction would show him only successively. He masses thus the separate\nelements of the solution, and by a sort of intuition divines before\nbeing able to demonstrate.\n\nTo divine before demonstrating! Need I recall that thus have been made\nall the important discoveries? How many are the truths that physical\nanalogies permit us to present and that we are not in condition to\nestablish by rigorous reasoning!\n\nFor example, mathematical physics introduces a great number of\ndevelopments in series. No one doubts that these developments converge;\nbut the mathematical certitude is lacking. These are so many conquests\nassured for the investigators who shall come after us.\n\nOn the other hand, physics furnishes us not alone solutions; it\nfurnishes us besides, in a certain measure, arguments. It will suffice\nto recall how Felix Klein, in a question relative to Riemann surfaces,\nhas had recourse to the properties of electric currents.\n\nIt is true, the arguments of this species are not rigorous, in the sense\nthe analyst attaches to this word. And here a question arises: How can a\ndemonstration not sufficiently rigorous for the analyst suffice for the\nphysicist? It seems there can not be two rigors, that rigor is or is\nnot, and that, where it is not there can not be deduction.\n\nThis apparent paradox will be better understood by recalling under what\nconditions number is applied to natural phenomena. Whence come in\ngeneral the difficulties encountered in seeking rigor? We strike them\nalmost always in seeking to establish that some quantity tends to some\nlimit, or that some function is continuous, or that it has a derivative.\n\nNow the numbers the physicist measures by experiment are never known\nexcept approximately; and besides, any function always differs as little\nas you choose from a discontinuous function, and at the same time it\ndiffers as little as you choose from a continuous function. The\nphysicist may, therefore, at will suppose that the function studied is\ncontinuous, or that it is discontinuous; that it has or has not a\nderivative; and may do so without fear of ever being contradicted,\neither by present experience or by any future experiment. We see that\nwith such liberty he makes sport of difficulties which stop the analyst.\nHe may always reason as if all the functions which occur in his\ncalculations were entire polynomials.\n\nThus the sketch which suffices for physics is not the deduction which\nanalysis requires. It does not follow thence that one can not aid in\nfinding the other. So many physical sketches have already been\ntransformed into rigorous demonstrations that to-day this transformation\nis easy. There would be plenty of examples did I not fear in citing them\nto tire the reader.\n\nI hope I have said enough to show that pure analysis and mathematical\nphysics may serve one another without making any sacrifice one to the\nother, and that each of these two sciences should rejoice in all which\nelevates its associate.\n\n\n\n\nCHAPTER VI\n\nASTRONOMY\n\n\nGovernments and parliaments must find that astronomy is one of the\nsciences which cost most dear: the least instrument costs hundreds of\nthousands of dollars, the least observatory costs millions; each eclipse\ncarries with it supplementary appropriations. And all that for stars\nwhich are so far away, which are complete strangers to our electoral\ncontests, and in all probability will never take any part in them. It\nmust be that our politicians have retained a remnant of idealism, a\nvague instinct for what is grand; truly, I think they have been\ncalumniated; they should be encouraged and shown that this instinct does\nnot deceive them, that they are not dupes of that idealism.\n\nWe might indeed speak to them of navigation, of which no one can\nunderestimate the importance, and which has need of astronomy. But this\nwould be to take the question by its smaller side.\n\nAstronomy is useful because it raises us above ourselves; it is useful\nbecause it is grand; that is what we should say. It shows us how small\nis man's body, how great his mind, since his intelligence can embrace\nthe whole of this dazzling immensity, where his body is only an obscure\npoint, and enjoy its silent harmony. Thus we attain the consciousness of\nour power, and this is something which can not cost too dear, since this\nconsciousness makes us mightier.\n\nBut what I should wish before all to show is, to what point astronomy\nhas facilitated the work of the other sciences, more directly useful,\nsince it has given us a soul capable of comprehending nature.\n\nThink how diminished humanity would be if, under heavens constantly\noverclouded, as Jupiter's must be, it had forever remained ignorant of\nthe stars. Do you think that in such a world we should be what we are? I\nknow well that under this somber vault we should have been deprived of\nthe light of the sun, necessary to organisms like those which inhabit\nthe earth. But if you please, we shall assume that these clouds are\nphosphorescent and emit a soft and constant light. Since we are making\nhypotheses, another will cost no more. Well! I repeat my question: Do\nyou think that in such a world we should be what we are?\n\nThe stars send us not only that visible and gross light which strikes\nour bodily eyes, but from them also comes to us a light far more subtle,\nwhich illuminates our minds and whose effects I shall try to show you.\nYou know what man was on the earth some thousands of years ago, and what\nhe is to-day. Isolated amidst a nature where everything was a mystery to\nhim, terrified at each unexpected manifestation of incomprehensible\nforces, he was incapable of seeing in the conduct of the universe\nanything but caprice; he attributed all phenomena to the action of a\nmultitude of little genii, fantastic and exacting, and to act on the\nworld he sought to conciliate them by means analogous to those employed\nto gain the good graces of a minister or a deputy. Even his failures did\nnot enlighten him, any more than to-day a beggar refused is discouraged\nto the point of ceasing to beg.\n\nTo-day we no longer beg of nature; we command her, because we have\ndiscovered certain of her secrets and shall discover others each day. We\ncommand her in the name of laws she can not challenge, because they are\nhers; these laws we do not madly ask her to change, we are the first to\nsubmit to them. Nature can only be governed by obeying her.\n\nWhat a change must our souls have undergone to pass from the one state\nto the other! Does any one believe that, without the lessons of the\nstars, under the heavens perpetually overclouded that I have just\nsupposed, they would have changed so quickly? Would the metamorphosis\nhave been possible, or at least would it not have been much slower?\n\nAnd first of all, astronomy it is which taught that there are laws. The\nChaldeans, who were the first to observe the heavens with some\nattention, saw that this multitude of luminous points is not a confused\ncrowd wandering at random, but rather a disciplined army. Doubtless the\nrules of this discipline escaped them, but the harmonious spectacle of\nthe starry night sufficed to give them the impression of regularity,\nand that was in itself already a great thing. Besides, these rules were\ndiscerned by Hipparchus, Ptolemy, Copernicus, Kepler, one after another,\nand finally, it is needless to recall that Newton it was who enunciated\nthe oldest, the most precise, the most simple, the most general of all\nnatural laws.\n\nAnd then, taught by this example, we have seen our little terrestrial\nworld better and, under the apparent disorder, there also we have found\nagain the harmony that the study of the heavens had revealed to us. It\nalso is regular, it also obeys immutable laws, but they are more\ncomplicated, in apparent conflict one with another, and an eye untrained\nby other sights would have seen there only chaos and the reign of chance\nor caprice. If we had not known the stars, some bold spirits might\nperhaps have sought to foresee physical phenomena; but their failures\nwould have been frequent, and they would have excited only the derision\nof the vulgar; do we not see, that even in our day the meteorologists\nsometimes deceive themselves, and that certain persons are inclined to\nlaugh at them.\n\nHow often would the physicists, disheartened by so many checks, have\nfallen into discouragement, if they had not had, to sustain their\nconfidence, the brilliant example of the success of the astronomers!\nThis success showed them that nature obeys laws; it only remained to\nknow what laws; for that they only needed patience, and they had the\nright to demand that the sceptics should give them credit.\n\nThis is not all: astronomy has not only taught us that there are laws,\nbut that from these laws there is no escape, that with them there is no\npossible compromise. How much time should we have needed to comprehend\nthat fact, if we had known only the terrestrial world, where each\nelemental force would always seem to us in conflict with other forces?\nAstronomy has taught us that the laws are infinitely precise, and that\nif those we enunciate are approximative, it is because we do not know\nthem well. Aristotle, the most scientific mind of antiquity, still\naccorded a part to accident, to chance, and seemed to think that the\nlaws of nature, at least here below, determine only the large features\nof phenomena. How much has the ever-increasing precision of\nastronomical predictions contributed to correct such an error, which\nwould have rendered nature unintelligible!\n\nBut are these laws not local, varying in different places, like those\nwhich men make; does not that which is truth in one corner of the\nuniverse, on our globe, for instance, or in our little solar system,\nbecome error a little farther away? And then could it not be asked\nwhether laws depending on space do not also depend upon time, whether\nthey are not simple habitudes, transitory, therefore, and ephemeral?\nAgain it is astronomy that answers this question. Consider the double\nstars; all describe conics; thus, as far as the telescope carries, it\ndoes not reach the limits of the domain which obeys Newton's law.\n\nEven the simplicity of this law is a lesson for us; how many complicated\nphenomena are contained in the two lines of its enunciation; persons who\ndo not understand celestial mechanics may form some idea of it at least\nfrom the size of the treatises devoted to this science; and then it may\nbe hoped that the complication of physical phenomena likewise hides from\nus some simple cause still unknown.\n\nIt is therefore astronomy which has shown us what are the general\ncharacteristics of natural laws; but among these characteristics there\nis one, the most subtle and the most important of all, which I shall ask\nleave to stress.\n\nHow was the order of the universe understood by the ancients; for\ninstance, by Pythagoras, Plato or Aristotle? It was either an immutable\ntype fixed once for all, or an ideal to which the world sought to\napproach. Kepler himself still thought thus when, for instance, he\nsought whether the distances of the planets from the sun had not some\nrelation to the five regular polyhedrons. This idea contained nothing\nabsurd, but it was sterile, since nature is not so made. Newton has\nshown us that a law is only a necessary relation between the present\nstate of the world and its immediately subsequent state. All the other\nlaws since discovered are nothing else; they are in sum, differential\nequations; but it is astronomy which furnished the first model for them,\nwithout which we should doubtless long have erred.\n\nAstronomy has also taught us to set at naught appearances. The day\nCopernicus proved that what was thought the most stable was in motion,\nthat what was thought moving was fixed, he showed us how deceptive could\nbe the infantile reasonings which spring directly from the immediate\ndata of our senses. True, his ideas did not easily triumph, but since\nthis triumph there is no longer a prejudice so inveterate that we can\nnot shake it off. How can we estimate the value of the new weapon thus\nwon?\n\nThe ancients thought everything was made for man, and this illusion must\nbe very tenacious, since it must ever be combated. Yet it is necessary\nto divest oneself of it; or else one will be only an eternal myope,\nincapable of seeing the truth. To comprehend nature one must be able to\nget out of self, so to speak, and to contemplate her from many different\npoints of view; otherwise we never shall know more than one side. Now,\nto get out of self is what he who refers everything to himself can not\ndo. Who delivered us from this illusion? It was those who showed us that\nthe earth is only one of the smallest planets of the solar system, and\nthat the solar system itself is only an imperceptible point in the\ninfinite spaces of the stellar universe.\n\nAt the same time astronomy taught us not to be afraid of big numbers.\nThis was needful, not only for knowing the heavens, but to know the\nearth itself; and was not so easy as it seems to us to-day. Let us try\nto go back and picture to ourselves what a Greek would have thought if\ntold that red light vibrates four hundred millions of millions of times\nper second. Without any doubt, such an assertion would have appeared to\nhim pure madness, and he never would have lowered himself to test it.\nTo-day a hypothesis will no longer appear absurd to us because it\nobliges us to imagine objects much larger or smaller than those our\nsenses are capable of showing us, and we no longer comprehend those\nscruples which arrested our predecessors and prevented them from\ndiscovering certain truths simply because they were afraid of them. But\nwhy? It is because we have seen the heavens enlarging and enlarging\nwithout cease; because we know that the sun is 150 millions of\nkilometers from the earth and that the distances of the nearest stars\nare hundreds of thousands of times greater yet. Habituated to the\ncontemplation of the infinitely great, we have become apt to comprehend\nthe infinitely small. Thanks to the education it has received, our\nimagination, like the eagle's eye that the sun does not dazzle, can look\ntruth in the face.\n\nWas I wrong in saying that it is astronomy which has made us a soul\ncapable of comprehending nature; that under heavens always overcast and\nstarless, the earth itself would have been for us eternally\nunintelligible; that we should there have seen only caprice and\ndisorder; and that, not knowing the world, we should never have been\nable to subdue it? What science could have been more useful? And in thus\nspeaking I put myself at the point of view of those who only value\npractical applications. Certainly, this point of view is not mine; as\nfor me, on the contrary, if I admire the conquests of industry, it is\nabove all because if they free us from material cares, they will one day\ngive to all the leisure to contemplate nature. I do not say: Science is\nuseful, because it teaches us to construct machines. I say: Machines are\nuseful, because in working for us, they will some day leave us more time\nto make science. But finally it is worth remarking that between the two\npoints of view there is no antagonism, and that man having pursued a\ndisinterested aim, all else has been added unto him.\n\nAuguste Comte has said somewhere, that it would be idle to seek to know\nthe composition of the sun, since this knowledge would be of no use to\nsociology. How could he be so short-sighted? Have we not just seen that\nit is by astronomy that, to speak his language, humanity has passed from\nthe theological to the positive state? He found an explanation for that\nbecause it had happened. But how has he not understood that what\nremained to do was not less considerable and would be not less\nprofitable? Physical astronomy, which he seems to condemn, has already\nbegun to bear fruit, and it will give us much more, for it only dates\nfrom yesterday.\n\nFirst was discovered the nature of the sun, what the founder of\npositivism wished to deny us, and there bodies were found which exist on\nthe earth, but had here remained undiscovered; for example, helium, that\ngas almost as light as hydrogen. That already contradicted Comte. But to\nthe spectroscope we owe a lesson precious in a quite different way; in\nthe most distant stars, it shows us the same substances. It might have\nbeen asked whether the terrestrial elements were not due to some chance\nwhich had brought together more tenuous atoms to construct of them the\nmore complex edifice that the chemists call atom; whether, in other\nregions of the universe, other fortuitous meetings had not engendered\nedifices entirely different. Now we know that this is not so, that the\nlaws of our chemistry are the general laws of nature, and that they owe\nnothing to the chance which caused us to be born on the earth.\n\nBut, it will be said, astronomy has given to the other sciences all it\ncan give them, and now that the heavens have procured for us the\ninstruments which enable us to study terrestrial nature, they could\nwithout danger veil themselves forever. After what we have just said, is\nthere still need to answer this objection? One could have reasoned the\nsame in Ptolemy's time; then also men thought they knew everything, and\nthey still had almost everything to learn.\n\nThe stars are majestic laboratories, gigantic crucibles, such as no\nchemist could dream. There reign temperatures impossible for us to\nrealize. Their only defect is being a little far away; but the telescope\nwill soon bring them near to us, and then we shall see how matter acts\nthere. What good fortune for the physicist and the chemist!\n\nMatter will there exhibit itself to us under a thousand different\nstates, from those rarefied gases which seem to form the nebul\u00e6 and\nwhich are luminous with I know not what glimmering of mysterious origin,\neven to the incandescent stars and to the planets so near and yet so\ndifferent.\n\nPerchance even, the stars will some day teach us something about life;\nthat seems an insensate dream and I do not at all see how it can be\nrealized; but, a hundred years ago, would not the chemistry of the stars\nhave also appeared a mad dream?\n\nBut limiting our views to horizons less distant, there still will remain\nto us promises less contingent and yet sufficiently seductive. If the\npast has given us much, we may rest assured that the future will give us\nstill more.\n\nIn sum, it is incredible how useful belief in astrology has been to\nhumanity. If Kepler and Tycho Brahe made a living, it was because they\nsold to na\u00efve kings predictions founded on the conjunctions of the\nstars. If these princes had not been so credulous, we should perhaps\nstill believe that nature obeys caprice, and we should still wallow in\nignorance.\n\n\n\n\nCHAPTER VII\n\nTHE HISTORY OF MATHEMATICAL PHYSICS\n\n\n_The Past and the Future of Physics._--What is the present state of\nmathematical physics? What are the problems it is led to set itself?\nWhat is its future? Is its orientation about to be modified?\n\nTen years hence will the aim and the methods of this science appear to\nour immediate successors in the same light as to ourselves; or, on the\ncontrary, are we about to witness a profound transformation? Such are\nthe questions we are forced to raise in entering to-day upon our\ninvestigation.\n\nIf it is easy to propound them: to answer is difficult. If we felt\ntempted to risk a prediction, we should easily resist this temptation,\nby thinking of all the stupidities the most eminent savants of a hundred\nyears ago would have uttered, if some one had asked them what the\nscience of the nineteenth century would be. They would have thought\nthemselves bold in their predictions, and after the event, how very\ntimid we should have found them. Do not, therefore, expect of me any\nprophecy.\n\nBut if, like all prudent physicians, I shun giving a prognosis, yet I\ncan not dispense with a little diagnostic; well, yes, there are\nindications of a serious crisis, as if we might expect an approaching\ntransformation. Still, be not too anxious: we are sure the patient will\nnot die of it, and we may even hope that this crisis will be salutary,\nfor the history of the past seems to guarantee us this. This crisis, in\nfact, is not the first, and to understand it, it is important to recall\nthose which have preceded. Pardon then a brief historical sketch.\n\n_The Physics of Central Forces._--Mathematical physics, as we know, was\nborn of celestial mechanics, which gave birth to it at the end of the\neighteenth century, at the moment when it itself attained its complete\ndevelopment. During its first years especially, the infant strikingly\nresembled its mother.\n\nThe astronomic universe is formed of masses, very great, no doubt, but\nseparated by intervals so immense that they appear to us only as\nmaterial points. These points attract each other inversely as the square\nof the distance, and this attraction is the sole force which influences\ntheir movements. But if our senses were sufficiently keen to show us all\nthe details of the bodies which the physicist studies, the spectacle\nthus disclosed would scarcely differ from the one the astronomer\ncontemplates. There also we should see material points, separated from\none another by intervals, enormous in comparison with their dimensions,\nand describing orbits according to regular laws. These infinitesimal\nstars are the atoms. Like the stars proper, they attract or repel each\nother, and this attraction or this repulsion, following the straight\nline which joins them, depends only on the distance. The law according\nto which this force varies as function of the distance is perhaps not\nthe law of Newton, but it is an analogous law; in place of the exponent\n-2, we have probably a different exponent, and it is from this change of\nexponent that arises all the diversity of physical phenomena, the\nvariety of qualities and of sensations, all the world, colored and\nsonorous, which surrounds us; in a word, all nature.\n\nSuch is the primitive conception in all its purity. It only remains to\nseek in the different cases what value should be given to this exponent\nin order to explain all the facts. It is on this model that Laplace, for\nexample, constructed his beautiful theory of capillarity; he regards it\nonly as a particular case of attraction, or, as he says, of universal\ngravitation, and no one is astonished to find it in the middle of one of\nthe five volumes of the 'M\u00e9canique c\u00e9leste.' More recently Briot\nbelieves he penetrated the final secret of optics in demonstrating that\nthe atoms of ether attract each other in the inverse ratio of the sixth\npower of the distance; and Maxwell himself, does he not say somewhere\nthat the atoms of gases repel each other in the inverse ratio of the\nfifth power of the distance? We have the exponent -6, or -5, in place of\nthe exponent -2, but it is always an exponent.\n\nAmong the theories of this epoch, one alone is an exception, that of\nFourier; in it are indeed atoms acting at a distance one upon the other;\nthey mutually transmit heat, but they do not attract, they never budge.\nFrom this point of view, Fourier's theory must have appeared to the eyes\nof his contemporaries, to those of Fourier himself, as imperfect and\nprovisional.\n\nThis conception was not without grandeur; it was seductive, and many\namong us have not finally renounced it; they know that one will attain\nthe ultimate elements of things only by patiently disentangling the\ncomplicated skein that our senses give us; that it is necessary to\nadvance step by step, neglecting no intermediary; that our fathers were\nwrong in wishing to skip stations; but they believe that when one shall\nhave arrived at these ultimate elements, there again will be found the\nmajestic simplicity of celestial mechanics.\n\nNeither has this conception been useless; it has rendered us an\ninestimable service, since it has contributed to make precise the\nfundamental notion of the physical law.\n\nI will explain myself; how did the ancients understand law? It was for\nthem an internal harmony, static, so to say, and immutable; or else it\nwas like a model that nature tried to imitate. For us a law is something\nquite different; it is a constant relation between the phenomenon of\nto-day and that of to-morrow; in a word, it is a differential equation.\n\nBehold the ideal form of physical law; well, it is Newton's law which\nfirst clothed it forth. If then one has acclimated this form in physics,\nit is precisely by copying as far as possible this law of Newton, that\nis by imitating celestial mechanics. This is, moreover, the idea I have\ntried to bring out in Chapter VI.\n\n_The Physics of the Principles._--Nevertheless, a day arrived when the\nconception of central forces no longer appeared sufficient, and this is\nthe first of those crises of which I just now spoke.\n\nWhat was done then? The attempt to penetrate into the detail of the\nstructure of the universe, to isolate the pieces of this vast mechanism,\nto analyze one by one the forces which put them in motion, was\nabandoned, and we were content to take as guides certain general\nprinciples the express object of which is to spare us this minute study.\nHow so? Suppose we have before us any machine; the initial wheel work\nand the final wheel work alone are visible, but the transmission, the\nintermediary machinery by which the movement is communicated from one to\nthe other, is hidden in the interior and escapes our view; we do not\nknow whether the communication is made by gearing or by belts, by\nconnecting-rods or by other contrivances. Do we say that it is\nimpossible for us to understand anything about this machine so long as\nwe are not permitted to take it to pieces? You know well we do not, and\nthat the principle of the conservation of energy suffices to determine\nfor us the most interesting point. We easily ascertain that the final\nwheel turns ten times less quickly than the initial wheel, since these\ntwo wheels are visible; we are able thence to conclude that a couple\napplied to the one will be balanced by a couple ten times greater\napplied to the other. For that there is no need to penetrate the\nmechanism of this equilibrium and to know how the forces compensate each\nother in the interior of the machine; it suffices to be assured that\nthis compensation can not fail to occur.\n\nWell, in regard to the universe, the principle of the conservation of\nenergy is able to render us the same service. The universe is also a\nmachine, much more complicated than all those of industry, of which\nalmost all the parts are profoundly hidden from us; but in observing the\nmotion of those that we can see, we are able, by the aid of this\nprinciple, to draw conclusions which remain true whatever may be the\ndetails of the invisible mechanism which animates them.\n\nThe principle of the conservation of energy, or Mayer's principle, is\ncertainly the most important, but it is not the only one; there are\nothers from which we can derive the same advantage. These are:\n\nCarnot's principle, or the principle of the degradation of energy.\n\nNewton's principle, or the principle of the equality of action and\nreaction.\n\nThe principle of relativity, according to which the laws of physical\nphenomena must be the same for a stationary observer as for an observer\ncarried along in a uniform motion of translation; so that we have not\nand can not have any means of discerning whether or not we are carried\nalong in such a motion.\n\nThe principle of the conservation of mass, or Lavoisier's principle.\n\nI will add the principle of least action.\n\nThe application of these five or six general principles to the different\nphysical phenomena is sufficient for our learning of them all that we\ncould reasonably hope to know of them. The most remarkable example of\nthis new mathematical physics is, beyond question, Maxwell's\nelectromagnetic theory of light.\n\nWe know nothing as to what the ether is, how its molecules are disposed,\nwhether they attract or repel each other; but we know that this medium\ntransmits at the same time the optical perturbations and the electrical\nperturbations; we know that this transmission must take place in\nconformity with the general principles of mechanics, and that suffices\nus for the establishment of the equations of the electromagnetic field.\n\nThese principles are results of experiments boldly generalized; but they\nseem to derive from their very generality a high degree of certainty. In\nfact, the more general they are, the more frequent are the opportunities\nto check them, and the verifications multiplying, taking the most\nvaried, the most unexpected forms, end by no longer leaving place for\ndoubt.\n\n_Utility of the Old Physics._--Such is the second phase of the history\nof mathematical physics and we have not yet emerged from it. Shall we\nsay that the first has been useless? that during fifty years science\nwent the wrong way, and that there is nothing left but to forget so many\naccumulated efforts that a vicious conception condemned in advance to\nfailure? Not the least in the world. Do you think the second phase could\nhave come into existence without the first? The hypothesis of central\nforces contained all the principles; it involved them as necessary\nconsequences; it involved both the conservation of energy and that of\nmasses, and the equality of action and reaction, and the law of least\naction, which appeared, it is true, not as experimental truths, but as\ntheorems; the enunciation of which had at the same time something more\nprecise and less general than under their present form.\n\nIt is the mathematical physics of our fathers which has familiarized us\nlittle by little with these various principles; which has habituated us\nto recognize them under the different vestments in which they disguise\nthemselves. They have been compared with the data of experience, it has\nbeen seen how it was necessary to modify their enunciation to adapt them\nto these data; thereby they have been extended and consolidated. Thus\nthey came to be regarded as experimental truths; the conception of\ncentral forces became then a useless support, or rather an\nembarrassment, since it made the principles partake of its hypothetical\ncharacter.\n\nThe frames then have not broken, because they are elastic; but they have\nenlarged; our fathers, who established them, did not labor in vain, and\nwe recognize in the science of to-day the general traits of the sketch\nwhich they traced.\n\n\n\n\nCHAPTER VIII\n\nTHE PRESENT CRISIS OF MATHEMATICAL PHYSICS\n\n\n_The New Crisis._--Are we now about to enter upon a third period? Are we\non the eve of a second crisis? These principles on which we have built\nall, are they about to crumble away in their turn? This has been for\nsome time a pertinent question.\n\nWhen I speak thus, you no doubt think of radium, that grand\nrevolutionist of the present time, and in fact I shall come back to it\npresently; but there is something else. It is not alone the conservation\nof energy which is in question; all the other principles are equally in\ndanger, as we shall see in passing them successively in review.\n\n_Carnot's Principle._--Let us commence with the principle of Carnot.\nThis is the only one which does not present itself as an immediate\nconsequence of the hypothesis of central forces; more than that, it\nseems, if not to directly contradict that hypothesis, at least not to be\nreconciled with it without a certain effort. If physical phenomena were\ndue exclusively to the movements of atoms whose mutual attraction\ndepended only on the distance, it seems that all these phenomena should\nbe reversible; if all the initial velocities were reversed, these atoms,\nalways subjected to the same forces, ought to go over their trajectories\nin the contrary sense, just as the earth would describe in the\nretrograde sense this same elliptic orbit which it describes in the\ndirect sense, if the initial conditions of its motion had been reversed.\nOn this account, if a physical phenomenon is possible, the inverse\nphenomenon should be equally so, and one should be able to reascend the\ncourse of time. Now, it is not so in nature, and this is precisely what\nthe principle of Carnot teaches us; heat can pass from the warm body to\nthe cold body; it is impossible afterward to make it take the inverse\nroute and to reestablish differences of temperature which have been\neffaced. Motion can be wholly dissipated and transformed into heat by\nfriction; the contrary transformation can never be made except\npartially.\n\nWe have striven to reconcile this apparent contradiction. If the world\ntends toward uniformity, this is not because its ultimate parts, at\nfirst unlike, tend to become less and less different; it is because,\nshifting at random, they end by blending. For an eye which should\ndistinguish all the elements, the variety would remain always as great;\neach grain of this dust preserves its originality and does not model\nitself on its neighbors; but as the blend becomes more and more\nintimate, our gross senses perceive only the uniformity. This is why,\nfor example, temperatures tend to a level, without the possibility of\ngoing backwards.\n\nA drop of wine falls into a glass of water; whatever may be the law of\nthe internal motion of the liquid, we shall soon see it colored of a\nuniform rosy tint, and however much from this moment one may shake it\nafterwards, the wine and the water do not seem capable of again\nseparating. Here we have the type of the irreversible physical\nphenomenon: to hide a grain of barley in a heap of wheat, this is easy;\nafterwards to find it again and get it out, this is practically\nimpossible. All this Maxwell and Boltzmann have explained; but the one\nwho has seen it most clearly, in a book too little read because it is a\nlittle difficult to read, is Gibbs, in his `Elementary Principles of\nStatistical Mechanics.'\n\nFor those who take this point of view, Carnot's principle is only an\nimperfect principle, a sort of concession to the infirmity of our\nsenses; it is because our eyes are too gross that we do not distinguish\nthe elements of the blend; it is because our hands are too gross that we\ncan not force them to separate; the imaginary demon of Maxwell, who is\nable to sort the molecules one by one, could well constrain the world to\nreturn backward. Can it return of itself? That is not impossible; that\nis only infinitely improbable. The chances are that we should wait a\nlong time for the concourse of circumstances which would permit a\nretrogradation; but sooner or later they will occur, after years whose\nnumber it would take millions of figures to write. These reservations,\nhowever, all remained theoretic; they were not very disquieting, and\nCarnot's principle retained all its practical value. But here the scene\nchanges. The biologist, armed with his microscope, long ago noticed in\nhis preparations irregular movements of little particles in suspension;\nthis is the Brownian movement. He first thought this was a vital\nphenomenon, but soon he saw that the inanimate bodies danced with no\nless ardor than the others; then he turned the matter over to the\nphysicists. Unhappily, the physicists remained long uninterested in this\nquestion; one concentrates the light to illuminate the microscopic\npreparation, thought they; with light goes heat; thence inequalities of\ntemperature and in the liquid interior currents which produce the\nmovements referred to. It occurred to M. Gouy to look more closely, and\nhe saw, or thought he saw, that this explanation is untenable, that the\nmovements become brisker as the particles are smaller, but that they are\nnot influenced by the mode of illumination. If then these movements\nnever cease, or rather are reborn without cease, without borrowing\nanything from an external source of energy, what ought we to believe? To\nbe sure, we should not on this account renounce our belief in the\nconservation of energy, but we see under our eyes now motion transformed\ninto heat by friction, now inversely heat changed into motion, and that\nwithout loss since the movement lasts forever. This is the contrary of\nCarnot's principle. If this be so, to see the world return backward, we\nno longer have need of the infinitely keen eye of Maxwell's demon; our\nmicroscope suffices. Bodies too large, those, for example, which are a\ntenth of a millimeter, are hit from all sides by moving atoms, but they\ndo not budge, because these shocks are very numerous and the law of\nchance makes them compensate each other; but the smaller particles\nreceive too few shocks for this compensation to take place with\ncertainty and are incessantly knocked about. And behold already one of\nour principles in peril.\n\n_The Principle of Relativity._--Let us pass to the principle of\nrelativity; this not only is confirmed by daily experience, not only is\nit a necessary consequence of the hypothesis of central forces, but it\nis irresistibly imposed upon our good sense, and yet it also is\nassailed. Consider two electrified bodies; though they seem to us at\nrest, they are both carried along by the motion of the earth; an\nelectric charge in motion, Rowland has taught us, is equivalent to a\ncurrent; these two charged bodies are, therefore, equivalent to two\nparallel currents of the same sense and these two currents should\nattract each other. In measuring this attraction, we shall measure the\nvelocity of the earth; not its velocity in relation to the sun or the\nfixed stars, but its absolute velocity.\n\nI well know what will be said: It is not its absolute velocity that is\nmeasured, it is its velocity in relation to the ether. How\nunsatisfactory that is! Is it not evident that from the principle so\nunderstood we could no longer infer anything? It could no longer tell us\nanything just because it would no longer fear any contradiction. If we\nsucceed in measuring anything, we shall always be free to say that this\nis not the absolute velocity, and if it is not the velocity in relation\nto the ether, it might always be the velocity in relation to some new\nunknown fluid with which we might fill space.\n\nIndeed, experiment has taken upon itself to ruin this interpretation of\nthe principle of relativity; all attempts to measure the velocity of the\nearth in relation to the ether have led to negative results. This time\nexperimental physics has been more faithful to the principle than\nmathematical physics; the theorists, to put in accord their other\ngeneral views, would not have spared it; but experiment has been\nstubborn in confirming it. The means have been varied; finally Michelson\npushed precision to its last limits; nothing came of it. It is precisely\nto explain this obstinacy that the mathematicians are forced to-day to\nemploy all their ingenuity.\n\nTheir task was not easy, and if Lorentz has got through it, it is only\nby accumulating hypotheses.\n\nThe most ingenious idea was that of local time. Imagine two observers\nwho wish to adjust their timepieces by optical signals; they exchange\nsignals, but as they know that the transmission of light is not\ninstantaneous, they are careful to cross them. When station B perceives\nthe signal from station A, its clock should not mark the same hour as\nthat of station A at the moment of sending the signal, but this hour\naugmented by a constant representing the duration of the transmission.\nSuppose, for example, that station A sends its signal when its clock\nmarks the hour _O_, and that station B perceives it when its clock marks\nthe hour _t_. The clocks are adjusted if the slowness equal to _t_\nrepresents the duration of the transmission, and to verify it, station B\nsends in its turn a signal when its clock marks _O_; then station A\nshould perceive it when its clock marks _t_. The timepieces are then\nadjusted.\n\nAnd in fact they mark the same hour at the same physical instant, but on\nthe one condition, that the two stations are fixed. Otherwise the\nduration of the transmission will not be the same in the two senses,\nsince the station A, for example, moves forward to meet the optical\nperturbation emanating from B, whereas the station B flees before the\nperturbation emanating from A. The watches adjusted in that way will not\nmark, therefore, the true time; they will mark what may be called the\n_local time_, so that one of them will be slow of the other. It matters\nlittle, since we have no means of perceiving it. All the phenomena which\nhappen at A, for example, will be late, but all will be equally so, and\nthe observer will not perceive it, since his watch is slow; so, as the\nprinciple of relativity requires, he will have no means of knowing\nwhether he is at rest or in absolute motion.\n\nUnhappily, that does not suffice, and complementary hypotheses are\nnecessary; it is necessary to admit that bodies in motion undergo a\nuniform contraction in the sense of the motion. One of the diameters of\nthe earth, for example, is shrunk by one two-hundred-millionth in\nconsequence of our planet's motion, while the other diameter retains its\nnormal length. Thus the last little differences are compensated. And\nthen, there is still the hypothesis about forces. Forces, whatever be\ntheir origin, gravity as well as elasticity, would be reduced in a\ncertain proportion in a world animated by a uniform translation; or,\nrather, this would happen for the components perpendicular to the\ntranslation; the components parallel would not change. Resume, then, our\nexample of two electrified bodies; these bodies repel each other, but at\nthe same time if all is carried along in a uniform translation, they are\nequivalent to two parallel currents of the same sense which attract each\nother. This electrodynamic attraction diminishes, therefore, the\nelectrostatic repulsion, and the total repulsion is feebler than if the\ntwo bodies were at rest. But since to measure this repulsion we must\nbalance it by another force, and all these other forces are reduced in\nthe same proportion, we perceive nothing. Thus all seems arranged, but\nare all the doubts dissipated? What would happen if one could\ncommunicate by non-luminous signals whose velocity of propagation\ndiffered from that of light? If, after having adjusted the watches by\nthe optical procedure, we wished to verify the adjustment by the aid of\nthese new signals, we should observe discrepancies which would render\nevident the common translation of the two stations. And are such signals\ninconceivable, if we admit with Laplace that universal gravitation is\ntransmitted a million times more rapidly than light?\n\nThus, the principle of relativity has been valiantly defended in these\nlatter times, but the very energy of the defense proves how serious was\nthe attack.\n\n_Newton's Principle._--Let us speak now of the principle of Newton, on\nthe equality of action and reaction. This is intimately bound up with\nthe preceding, and it seems indeed that the fall of the one would\ninvolve that of the other. Thus we must not be astonished to find here\nthe same difficulties.\n\nElectrical phenomena, according to the theory of Lorentz, are due to the\ndisplacements of little charged particles, called electrons, immersed in\nthe medium we call ether. The movements of these electrons produce\nperturbations in the neighboring ether; these perturbations propagate\nthemselves in every direction with the velocity of light, and in turn\nother electrons, originally at rest, are made to vibrate when the\nperturbation reaches the parts of the ether which touch them. The\nelectrons, therefore, act on one another, but this action is not direct,\nit is accomplished through the ether as intermediary. Under these\nconditions can there be compensation between action and reaction, at\nleast for an observer who should take account only of the movements of\nmatter, that is, of the electrons, and who should be ignorant of those\nof the ether that he could not see? Evidently not. Even if the\ncompensation should be exact, it could not be simultaneous. The\nperturbation is propagated with a finite velocity; it, therefore,\nreaches the second electron only when the first has long ago entered\nupon its rest. This second electron, therefore, will undergo, after a\ndelay, the action of the first, but will certainly not at that moment\nreact upon it, since around this first electron nothing any longer\nbudges.\n\nThe analysis of the facts permits us to be still more precise. Imagine,\nfor example, a Hertzian oscillator, like those used in wireless\ntelegraphy; it sends out energy in every direction; but we can provide\nit with a parabolic mirror, as Hertz did with his smallest oscillators,\nso as to send all the energy produced in a single direction. What\nhappens then according to the theory? The apparatus recoils, as if it\nwere a cannon and the projected energy a ball; and that is contrary to\nthe principle of Newton, since our projectile here has no mass, it is\nnot matter, it is energy. The case is still the same, moreover, with a\nbeacon light provided with a reflector, since light is nothing but a\nperturbation of the electromagnetic field. This beacon light should\nrecoil as if the light it sends out were a projectile. What is the force\nthat should produce this recoil? It is what is called the\nMaxwell-Bartholi pressure. It is very minute, and it has been difficult\nto put it in evidence even with the most sensitive radiometers; but it\nsuffices that it exists.\n\nIf all the energy issuing from our oscillator falls on a receiver, this\nwill act as if it had received a mechanical shock, which will represent\nin a sense the compensation of the oscillator's recoil; the reaction\nwill be equal to the action, but it will not be simultaneous; the\nreceiver will move on, but not at the moment when the oscillator\nrecoils. If the energy propagates itself indefinitely without\nencountering a receiver, the compensation will never occur.\n\nShall we say that the space which separates the oscillator from the\nreceiver and which the perturbation must pass over in going from the one\nto the other is not void, that it is full not only of ether, but of air,\nor even in the interplanetary spaces of some fluid subtile but still\nponderable; that this matter undergoes the shock like the receiver at\nthe moment when the energy reaches it, and recoils in its turn when the\nperturbation quits it? That would save Newton's principle, but that is\nnot true. If energy in its diffusion remained always attached to some\nmaterial substratum, then matter in motion would carry along light with\nit, and Fizeau has demonstrated that it does nothing of the sort, at\nleast for air. Michelson and Morley have since confirmed this. It might\nbe supposed also that the movements of matter proper are exactly\ncompensated by those of the ether; but that would lead us to the same\nreflections as before now. The principle so understood will explain\neverything, since, whatever might be the visible movements, we always\ncould imagine hypothetical movements which compensate them. But if it is\nable to explain everything, this is because it does not enable us to\nforesee anything; it does not enable us to decide between the different\npossible hypotheses, since it explains everything beforehand. It\ntherefore becomes useless.\n\nAnd then the suppositions that it would be necessary to make on the\nmovements of the ether are not very satisfactory. If the electric\ncharges double, it would be natural to imagine that the velocities of\nthe diverse atoms of ether double also; but, for the compensation, it\nwould be necessary that the mean velocity of the ether quadruple.\n\nThis is why I have long thought that these consequences of theory,\ncontrary to Newton's principle, would end some day by being abandoned,\nand yet the recent experiments on the movements of the electrons issuing\nfrom radium seem rather to confirm them.\n\n_Lavoisier's Principle._--I arrive at the principle of Lavoisier on the\nconservation of mass. Certainly, this is one not to be touched without\nunsettling all mechanics. And now certain persons think that it seems\ntrue to us only because in mechanics merely moderate velocities are\nconsidered, but that it would cease to be true for bodies animated by\nvelocities comparable to that of light. Now these velocities are\nbelieved at present to have been realized; the cathode rays and those of\nradium may be formed of very minute particles or of electrons which are\ndisplaced with velocities smaller no doubt than that of light, but which\nmight be its one tenth or one third.\n\nThese rays can be deflected, whether by an electric field, or by a\nmagnetic field, and we are able, by comparing these deflections, to\nmeasure at the same time the velocity of the electrons and their mass\n(or rather the relation of their mass to their charge). But when it was\nseen that these velocities approached that of light, it was decided that\na correction was necessary. These molecules, being electrified, can not\nbe displaced without agitating the ether; to put them in motion it is\nnecessary to overcome a double inertia, that of the molecule itself and\nthat of the ether. The total or apparent mass that one measures is\ncomposed, therefore, of two parts: the real or mechanical mass of the\nmolecule and the electrodynamic mass representing the inertia of the\nether.\n\nThe calculations of Abraham and the experiments of Kaufmann have then\nshown that the mechanical mass, properly so called, is null, and that\nthe mass of the electrons, or, at least, of the negative electrons, is\nof exclusively electrodynamic origin. This is what forces us to change\nthe definition of mass; we can not any longer distinguish mechanical\nmass and electrodynamic mass, since then the first would vanish; there\nis no mass other than electrodynamic inertia. But in this case the mass\ncan no longer be constant; it augments with the velocity, and it even\ndepends on the direction, and a body animated by a notable velocity will\nnot oppose the same inertia to the forces which tend to deflect it from\nits route, as to those which tend to accelerate or to retard its\nprogress.\n\nThere is still a resource; the ultimate elements of bodies are\nelectrons, some charged negatively, the others charged positively. The\nnegative electrons have no mass, this is understood; but the positive\nelectrons, from the little we know of them, seem much greater. Perhaps\nthey have, besides their electrodynamic mass, a true mechanical mass.\nThe real mass of a body would, then, be the sum of the mechanical masses\nof its positive electrons, the negative electrons not counting; mass so\ndefined might still be constant.\n\nAlas! this resource also evades us. Recall what we have said of the\nprinciple of relativity and of the efforts made to save it. And it is\nnot merely a principle which it is a question of saving, it is the\nindubitable results of the experiments of Michelson.\n\nWell, as was above seen, Lorentz, to account for these results, was\nobliged to suppose that all forces, whatever their origin, were reduced\nin the same proportion in a medium animated by a uniform translation;\nthis is not sufficient; it is not enough that this take place for the\nreal forces, it must also be the same for the forces of inertia; it is\ntherefore necessary, he says, that _the masses of all the particles be\ninfluenced by a translation to the same degree as the electromagnetic\nmasses of the electrons_.\n\nSo the mechanical masses must vary in accordance with the same laws as\nthe electrodynamic masses; they can not, therefore, be constant.\n\nNeed I point out that the fall of Lavoisier's principle involves that of\nNewton's? This latter signifies that the center of gravity of an\nisolated system moves in a straight line; but if there is no longer a\nconstant mass, there is no longer a center of gravity, we no longer know\neven what this is. This is why I said above that the experiments on the\ncathode rays appeared to justify the doubts of Lorentz concerning\nNewton's principle.\n\nFrom all these results, if they were confirmed, would arise an entirely\nnew mechanics, which would be, above all, characterized by this fact,\nthat no velocity could surpass that of light,[9] any more than any\ntemperature can fall below absolute zero.\n\n [9] Because bodies would oppose an increasing inertia to the causes\n which would tend to accelerate their motion; and this inertia\n would become infinite when one approached the velocity of light.\n\nNo more for an observer, carried along himself in a translation he does\nnot suspect, could any apparent velocity surpass that of light; and this\nwould be then a contradiction, if we did not recall that this observer\nwould not use the same clocks as a fixed observer, but, indeed, clocks\nmarking 'local time.'\n\nHere we are then facing a question I content myself with stating. If\nthere is no longer any mass, what becomes of Newton's law? Mass has two\naspects: it is at the same time a coefficient of inertia and an\nattracting mass entering as factor into Newtonian attraction. If the\ncoefficient of inertia is not constant, can the attracting mass be? That\nis the question.\n\n_Mayer's Principle._--At least, the principle of the conservation of\nenergy yet remained to us, and this seemed more solid. Shall I recall to\nyou how it was in its turn thrown into discredit? This event has made\nmore noise than the preceding, and it is in all the memoirs. From the\nfirst words of Becquerel, and, above all, when the Curies had discovered\nradium, it was seen that every radioactive body was an inexhaustible\nsource of radiation. Its activity seemed to subsist without alteration\nthroughout the months and the years. This was in itself a strain on the\nprinciples; these radiations were in fact energy, and from the same\nmorsel of radium this issued and forever issued. But these quantities of\nenergy were too slight to be measured; at least that was the belief and\nwe were not much disquieted.\n\nThe scene changed when Curie bethought himself to put radium in a\ncalorimeter; it was then seen that the quantity of heat incessantly\ncreated was very notable.\n\nThe explanations proposed were numerous; but in such case we can not\nsay, the more the better. In so far as no one of them has prevailed over\nthe others, we can not be sure there is a good one among them. Since\nsome time, however, one of these explanations seems to be getting the\nupper hand and we may reasonably hope that we hold the key to the\nmystery.\n\nSir W. Ramsay has striven to show that radium is in process of\ntransformation, that it contains a store of energy enormous but not\ninexhaustible. The transformation of radium then would produce a million\ntimes more heat than all known transformations; radium would wear itself\nout in 1,250 years; this is quite short, and you see that we are at\nleast certain to have this point settled some hundreds of years from\nnow. While waiting, our doubts remain.\n\n\n\n\nCHAPTER IX\n\nTHE FUTURE OF MATHEMATICAL PHYSICS\n\n\n_The Principles and Experiment._--In the midst of so much ruin, what\nremains standing? The principle of least action is hitherto intact, and\nLarmor appears to believe that it will long survive the others; in\nreality, it is still more vague and more general.\n\nIn presence of this general collapse of the principles, what attitude\nwill mathematical physics take? And first, before too much excitement,\nit is proper to ask if all that is really true. All these derogations to\nthe principles are encountered only among infinitesimals; the microscope\nis necessary to see the Brownian movement; electrons are very light;\nradium is very rare, and one never has more than some milligrams of it\nat a time. And, then, it may be asked whether, besides the infinitesimal\nseen, there was not another infinitesimal unseen counterpoise to the\nfirst.\n\nSo there is an interlocutory question, and, as it seems, only experiment\ncan solve it. We shall, therefore, only have to hand over the matter to\nthe experimenters, and, while waiting for them to finally decide the\ndebate, not to preoccupy ourselves with these disquieting problems, and\nto tranquilly continue our work as if the principles were still\nuncontested. Certes, we have much to do without leaving the domain where\nthey may be applied in all security; we have enough to employ our\nactivity during this period of doubts.\n\n_The R\u00f4le of the Analyst._--And as to these doubts, is it indeed true\nthat we can do nothing to disembarrass science of them? It must indeed\nbe said, it is not alone experimental physics that has given birth to\nthem; mathematical physics has well contributed. It is the experimenters\nwho have seen radium throw out energy, but it is the theorists who have\nput in evidence all the difficulties raised by the propagation of light\nacross a medium in motion; but for these it is probable we should not\nhave become conscious of them. Well, then, if they have done their best\nto put us into this embarrassment, it is proper also that they help us\nto get out of it.\n\nThey must subject to critical examination all these new views I have\njust outlined before you, and abandon the principles only after having\nmade a loyal effort to save them. What can they do in this sense? That\nis what I will try to explain.\n\nIt is a question before all of endeavoring to obtain a more satisfactory\ntheory of the electrodynamics of bodies in motion. It is there\nespecially, as I have sufficiently shown above, that difficulties\naccumulate. It is useless to heap up hypotheses, we can not satisfy all\nthe principles at once; so far, one has succeeded in safeguarding some\nonly on condition of sacrificing the others; but all hope of obtaining\nbetter results is not yet lost. Let us take, then, the theory of\nLorentz, turn it in all senses, modify it little by little, and perhaps\neverything will arrange itself.\n\nThus in place of supposing that bodies in motion undergo a contraction\nin the sense of the motion, and that this contraction is the same\nwhatever be the nature of these bodies and the forces to which they are\notherwise subjected, could we not make a more simple and natural\nhypothesis? We might imagine, for example, that it is the ether which is\nmodified when it is in relative motion in reference to the material\nmedium which penetrates it, that, when it is thus modified, it no longer\ntransmits perturbations with the same velocity in every direction. It\nmight transmit more rapidly those which are propagated parallel to the\nmotion of the medium, whether in the same sense or in the opposite\nsense, and less rapidly those which are propagated perpendicularly. The\nwave surfaces would no longer be spheres, but ellipsoids, and we could\ndispense with that extraordinary contraction of all bodies.\n\nI cite this only as an example, since the modifications that might be\nessayed would be evidently susceptible of infinite variation.\n\n_Aberration and Astronomy._--It is possible also that astronomy may some\nday furnish us data on this point; she it was in the main who raised the\nquestion in making us acquainted with the phenomenon of the aberration\nof light. If we make crudely the theory of aberration, we reach a very\ncurious result. The apparent positions of the stars differ from their\nreal positions because of the earth's motion, and as this motion is\nvariable, these apparent positions vary. The real position we can not\nascertain, but we can observe the variations of the apparent position.\nThe observations of the aberration show us, therefore, not the earth's\nmotion, but the variations of this motion; they can not, therefore, give\nus information about the absolute motion of the earth.\n\nAt least this is true in first approximation, but the case would be no\nlonger the same if we could appreciate the thousandths of a second. Then\nit would be seen that the amplitude of the oscillation depends not alone\non the variation of the motion, a variation which is well known, since\nit is the motion of our globe on its elliptic orbit, but on the mean\nvalue of this motion, so that the constant of aberration would not be\nquite the same for all the stars, and the differences would tell us the\nabsolute motion of the earth in space.\n\nThis, then, would be, under another form, the ruin of the principle of\nrelativity. We are far, it is true, from appreciating the thousandth of\na second, but, after all, say some, the earth's total absolute velocity\nis perhaps much greater than its relative velocity with respect to the\nsun. If, for example, it were 300 kilometers per second in place of 30,\nthis would suffice to make the phenomenon observable.\n\nI believe that in reasoning thus one admits a too simple theory of\naberration. Michelson has shown us, I have told you, that the physical\nprocedures are powerless to put in evidence absolute motion; I am\npersuaded that the same will be true of the astronomic procedures,\nhowever far precision be carried.\n\nHowever that may be, the data astronomy will furnish us in this regard\nwill some day be precious to the physicist. Meanwhile, I believe that\nthe theorists, recalling the experience of Michelson, may anticipate a\nnegative result, and that they would accomplish a useful work in\nconstructing a theory of aberration which would explain this in advance.\n\n_Electrons and Spectra._--This dynamics of electrons can be approached\nfrom many sides, but among the ways leading thither is one which has\nbeen somewhat neglected, and yet this is one of those which promise us\nthe most surprises. It is movements of electrons which produce the lines\nof the emission spectra; this is proved by the Zeeman effect; in an\nincandescent body what vibrates is sensitive to the magnet, therefore\nelectrified. This is a very important first point, but no one has gone\nfarther. Why are the lines of the spectrum distributed in accordance\nwith a regular law? These laws have been studied by the experimenters in\ntheir least details; they are very precise and comparatively simple. A\nfirst study of these distributions recalls the harmonics encountered in\nacoustics; but the difference is great. Not only are the numbers of\nvibrations not the successive multiples of a single number, but we do\nnot even find anything analogous to the roots of those transcendental\nequations to which we are led by so many problems of mathematical\nphysics: that of the vibrations of an elastic body of any form, that of\nthe Hertzian oscillations in a generator of any form, the problem of\nFourier for the cooling of a solid body.\n\nThe laws are simpler, but they are of wholly other nature, and to cite\nonly one of these differences, for the harmonics of high order, the\nnumber of vibrations tends toward a finite limit, instead of increasing\nindefinitely.\n\nThat has not yet been accounted for, and I believe that there we have\none of the most important secrets of nature. A Japanese physicist, M.\nNagaoka, has recently proposed an explanation; according to him, atoms\nare composed of a large positive electron surrounded by a ring formed of\na great number of very small negative electrons. Such is the planet\nSaturn with its rings. This is a very interesting attempt, but not yet\nwholly satisfactory; this attempt should be renewed. We will penetrate,\nso to speak, into the inmost recess of matter. And from the particular\npoint of view which we to-day occupy, when we know why the vibrations of\nincandescent bodies differ thus from ordinary elastic vibrations, why\nthe electrons do not behave like the matter which is familiar to us, we\nshall better comprehend the dynamics of electrons and it will be perhaps\nmore easy for us to reconcile it with the principles.\n\n_Conventions Preceding Experiment._--Suppose, now, that all these\nefforts fail, and, after all, I do not believe they will, what must be\ndone? Will it be necessary to seek to mend the broken principles by\ngiving what we French call a _coup de pouce_? That evidently is always\npossible, and I retract nothing of what I have said above.\n\nHave you not written, you might say if you wished to seek a quarrel with\nme--have you not written that the principles, though of experimental\norigin, are now unassailable by experiment because they have become\nconventions? And now you have just told us that the most recent\nconquests of experiment put these principles in danger.\n\nWell, formerly I was right and to-day I am not wrong. Formerly I was\nright, and what is now happening is a new proof of it. Take, for\nexample, the calorimetric experiment of Curie on radium. Is it possible\nto reconcile it with the principle of the conservation of energy? This\nhas been attempted in many ways. But there is among them one I should\nlike you to notice; this is not the explanation which tends to-day to\nprevail, but it is one of those which have been proposed. It has been\nconjectured that radium was only an intermediary, that it only stored\nradiations of unknown nature which flashed through space in every\ndirection, traversing all bodies, save radium, without being altered by\nthis passage and without exercising any action upon them. Radium alone\ntook from them a little of their energy and afterward gave it out to us\nin various forms.\n\nWhat an advantageous explanation, and how convenient! First, it is\nunverifiable and thus irrefutable. Then again it will serve to account\nfor any derogation whatever to Mayer's principle; it answers in advance\nnot only the objection of Curie, but all the objections that future\nexperimenters might accumulate. This new and unknown energy would serve\nfor everything.\n\nThis is just what I said, and therewith we are shown that our principle\nis unassailable by experiment.\n\nBut then, what have we gained by this stroke? The principle is intact,\nbut thenceforth of what use is it? It enabled us to foresee that in such\nor such circumstance we could count on such a total quantity of energy;\nit limited us; but now that this indefinite provision of new energy is\nplaced at our disposal, we are no longer limited by anything; and, as I\nhave written in 'Science and Hypothesis,' if a principle ceases to be\nfecund, experiment without contradicting it directly will nevertheless\nhave condemned it.\n\n_Future Mathematical Physics._--This, therefore, is not what would have\nto be done; it would be necessary to rebuild anew. If we were reduced to\nthis necessity; we could moreover console ourselves. It would not be\nnecessary thence to conclude that science can weave only a Penelope's\nweb, that it can raise only ephemeral structures, which it is soon\nforced to demolish from top to bottom with its own hands.\n\nAs I have said, we have already passed through a like crisis. I have\nshown you that in the second mathematical physics, that of the\nprinciples, we find traces of the first, that of central forces; it will\nbe just the same if we must know a third. Just so with the animal that\nexuviates, that breaks its too narrow carapace and makes itself a fresh\none; under the new envelope one will recognize the essential traits of\nthe organism which have persisted.\n\nWe can not foresee in what way we are about to expand; perhaps it is the\nkinetic theory of gases which is about to undergo development and serve\nas model to the others. Then the facts which first appeared to us as\nsimple thereafter would be merely resultants of a very great number of\nelementary facts which only the laws of chance would make cooperate for\na common end. Physical law would then assume an entirely new aspect; it\nwould no longer be solely a differential equation, it would take the\ncharacter of a statistical law.\n\nPerhaps, too, we shall have to construct an entirely new mechanics that\nwe only succeed in catching a glimpse of, where, inertia increasing with\nthe velocity, the velocity of light would become an impassable limit.\nThe ordinary mechanics, more simple, would remain a first approximation,\nsince it would be true for velocities not too great, so that the old\ndynamics would still be found under the new. We should not have to\nregret having believed in the principles, and even, since velocities too\ngreat for the old formulas would always be only exceptional, the surest\nway in practise would be still to act as if we continued to believe in\nthem. They are so useful, it would be necessary to keep a place for\nthem. To determine to exclude them altogether would be to deprive\noneself of a precious weapon. I hasten to say in conclusion that we are\nnot yet there, and as yet nothing proves that the principles will not\ncome forth from out the fray victorious and intact.[10]\n\n [10] These considerations on mathematical physics are borrowed from\n my St. Louis address.\n\n\n\n\nPART III\n\n\nTHE OBJECTIVE VALUE OF SCIENCE\n\n\n\n\nCHAPTER X\n\nIS SCIENCE ARTIFICIAL?\n\n\n1. _The Philosophy of M. LeRoy_\n\nThere are many reasons for being sceptics; should we push this\nscepticism to the very end or stop on the way? To go to the end is the\nmost tempting solution, the easiest and that which many have adopted,\ndespairing of saving anything from the shipwreck.\n\nAmong the writings inspired by this tendency it is proper to place in\nthe first rank those of M. LeRoy. This thinker is not only a philosopher\nand a writer of the greatest merit, but he has acquired a deep knowledge\nof the exact and physical sciences, and even has shown rare powers of\nmathematical invention. Let us recapitulate in a few words his doctrine,\nwhich has given rise to numerous discussions.\n\nScience consists only of conventions, and to this circumstance solely\ndoes it owe its apparent certitude; the facts of science and, _a\nfortiori_, its laws are the artificial work of the scientist; science\ntherefore can teach us nothing of the truth; it can only serve us as\nrule of action.\n\nHere we recognize the philosophic theory known under the name of\nnominalism; all is not false in this theory; its legitimate domain must\nbe left it, but out of this it should not be allowed to go.\n\nThis is not all; M. LeRoy's doctrine is not only nominalistic; it has\nbesides another characteristic which it doubtless owes to M. Bergson, it\nis anti-intellectualistic. According to M. LeRoy, the intellect deforms\nall it touches, and that is still more true of its necessary instrument\n'discourse.' There is reality only in our fugitive and changing\nimpressions, and even this reality, when touched, vanishes.\n\nAnd yet M. LeRoy is not a sceptic; if he regards the intellect as\nincurably powerless, it is only to give more scope to other sources of\nknowledge, to the heart, for instance, to sentiment, to instinct or to\nfaith.\n\nHowever great my esteem for M. LeRoy's talent, whatever the ingenuity of\nthis thesis, I can not wholly accept it. Certes, I am in accord on many\npoints with M. LeRoy, and he has even cited, in support of his view,\nvarious passages of my writings which I am by no means disposed to\nreject. I think myself only the more bound to explain why I can not go\nwith him all the way.\n\nM. LeRoy often complains of being accused of scepticism. He could not\nhelp being, though this accusation is probably unjust. Are not\nappearances against him? Nominalist in doctrine, but realist at heart,\nhe seems to escape absolute nominalism only by a desperate act of faith.\n\nThe fact is that anti-intellectualistic philosophy in rejecting analysis\nand 'discourse,' just by that condemns itself to being intransmissible;\nit is a philosophy essentially internal, or, at the very least, only its\nnegations can be transmitted; what wonder then that for an external\nobserver it takes the shape of scepticism?\n\nTherein lies the weak point of this philosophy; if it strives to remain\nfaithful to itself, its energy is spent in a negation and a cry of\nenthusiasm. Each author may repeat this negation and this cry, may vary\ntheir form, but without adding anything.\n\nAnd, yet, would it not be more logical in remaining silent? See, you\nhave written long articles; for that, it was necessary to use words. And\ntherein have you not been much more 'discursive' and consequently much\nfarther from life and truth than the animal who simply lives without\nphilosophizing? Would not this animal be the true philosopher?\n\nHowever, because no painter has made a perfect portrait, should we\nconclude that the best painting is not to paint? When a zoologist\ndissects an animal, certainly he 'alters it.' Yes, in dissecting it, he\ncondemns himself to never know all of it; but in not dissecting it, he\nwould condemn himself to never know anything of it and consequently to\nnever see anything of it.\n\nCertes, in man are other forces besides his intellect; no one has ever\nbeen mad enough to deny that. The first comer makes these blind forces\nact or lets them act; the philosopher must _speak_ of them; to speak of\nthem, he must know of them the little that can be known, he should\ntherefore _see_ them act. How? With what eyes, if not with his\nintellect? Heart, instinct, may guide it, but not render it useless;\nthey may direct the look, but not replace the eye. It may be granted\nthat the heart is the workman, and the intellect only the instrument.\nYet is it an instrument not to be done without, if not for action, at\nleast for philosophizing? Therefore a philosopher really\nanti-intellectualistic is impossible. Perhaps we shall have to declare\nfor the supremacy of action; always it is our intellect which will thus\nconclude; in allowing precedence to action it will thus retain the\nsuperiority of the thinking reed. This also is a supremacy not to be\ndisdained.\n\nPardon these brief reflections and pardon also their brevity, scarcely\nskimming the question. The process of intellectualism is not the subject\nI wish to treat: I wish to speak of science, and about it there is no\ndoubt; by definition, so to speak, it will be intellectualistic or it\nwill not be at all. Precisely the question is, whether it will be.\n\n\n2. _Science, Rule of Action_\n\nFor M. LeRoy, science is only a rule of action. We are powerless to know\nanything and yet we are launched, we must act, and at all hazards we\nhave established rules. It is the aggregate of these rules that is\ncalled science.\n\nIt is thus that men, desirous of diversion, have instituted rules of\nplay, like those of tric-trac for instance, which, better than science\nitself, could rely upon the proof by universal consent. It is thus\nlikewise that, unable to choose, but forced to choose, we toss up a\ncoin, head or tail to win.\n\nThe rule of tric-trac is indeed a rule of action like science, but does\nany one think the comparison just and not see the difference? The rules\nof the game are arbitrary conventions and the contrary convention might\nhave been adopted, _which would have been none the less good_. On the\ncontrary, science is a rule of action which is successful, generally at\nleast, and I add, while the contrary rule would not have succeeded.\n\nIf I say, to make hydrogen cause an acid to act on zinc, I formulate a\nrule which succeeds; I could have said, make distilled water act on\ngold; that also would have been a rule, only it would not have\nsucceeded. If, therefore, scientific 'recipes' have a value, as rule of\naction, it is because we know they succeed, generally at least. But to\nknow this is to know something and then why tell us we can know nothing?\n\nScience foresees, and it is because it foresees that it can be useful\nand serve as rule of action. I well know that its previsions are often\ncontradicted by the event; that shows that science is imperfect, and if\nI add that it will always remain so, I am certain that this is a\nprevision which, at least, will never be contradicted. Always the\nscientist is less often mistaken than a prophet who should predict at\nrandom. Besides the progress though slow is continuous, so that\nscientists, though more and more bold, are less and less misled. This is\nlittle, but it is enough.\n\nI well know that M. LeRoy has somewhere said that science was mistaken\noftener than one thought, that comets sometimes played tricks on\nastronomers, that scientists, who apparently are men, did not willingly\nspeak of their failures, and that, if they should speak of them, they\nwould have to count more defeats than victories.\n\nThat day, M. LeRoy evidently overreached himself. If science did not\nsucceed, it could not serve as rule of action; whence would it get its\nvalue? Because it is 'lived,' that is, because we love it and believe in\nit? The alchemists had recipes for making gold, they loved them and had\nfaith in them, and yet our recipes are the good ones, although our faith\nbe less lively, because they succeed.\n\nThere is no escape from this dilemma; either science does not enable us\nto foresee, and then it is valueless as rule of action; or else it\nenables us to foresee, in a fashion more or less imperfect, and then it\nis not without value as means of knowledge.\n\nIt should not even be said that action is the goal of science; should we\ncondemn studies of the star Sirius, under pretext that we shall probably\nnever exercise any influence on that star? To my eyes, on the contrary,\nit is the knowledge which is the end, and the action which is the means.\nIf I felicitate myself on the industrial development, it is not alone\nbecause it furnishes a facile argument to the advocates of science; it\nis above all because it gives to the scientist faith in himself and also\nbecause it offers him an immense field of experience where he clashes\nagainst forces too colossal to be tampered with. Without this ballast,\nwho knows whether he would not quit solid ground, seduced by the mirage\nof some scholastic novelty, or whether he would not despair, believing\nhe had fashioned only a dream?\n\n\n3. _The Crude Fact and the Scientific Fact_\n\nWhat was most paradoxical in M. LeRoy's thesis was that affirmation that\n_the scientist creates the fact_; this was at the same time its\nessential point and it is one of those which have been most discussed.\n\nPerhaps, says he (I well believe that this was a concession), it is not\nthe scientist that creates the fact in the rough; it is at least he who\ncreates the scientific fact.\n\nThis distinction between the fact in the rough and the scientific fact\ndoes not by itself appear to me illegitimate. But I complain first that\nthe boundary has not been traced either exactly or precisely; and then\nthat the author has seemed to suppose that the crude fact, not being\nscientific, is outside of science.\n\nFinally, I can not admit that the scientist creates without restraint\nthe scientific fact, since it is the crude fact which imposes it upon\nhim.\n\nThe examples given by M. LeRoy have greatly astonished me. The first is\ntaken from the notion of atom. The atom chosen as example of fact! I\navow that this choice has so disconcerted me that I prefer to say\nnothing about it. I have evidently misunderstood the author's thought\nand I could not fruitfully discuss it.\n\nThe second case taken as example is that of an eclipse where the crude\nphenomenon is a play of light and shadow, but where the astronomer can\nnot intervene without introducing two foreign elements, to wit, a clock\nand Newton's law.\n\nFinally, M. LeRoy cites the rotation of the earth; it has been answered:\nbut this is not a fact, and he has replied: it was one for Galileo, who\naffirmed it, as for the inquisitor, who denied it. It always remains\nthat this is not a fact in the same sense as those just spoken of and\nthat to give them the same name is to expose one's self to many\nconfusions.\n\nHere then are four degrees:\n\n1\u00ba. It grows dark, says the clown.\n\n2\u00ba. The eclipse happened at nine o'clock, says the astronomer.\n\n3\u00ba. The eclipse happened at the time deducible from the tables\nconstructed according to Newton's law, says he again.\n\n4\u00ba. That results from the earth's turning around the sun, says Galileo\nfinally.\n\nWhere then is the boundary between the fact in the rough and the\nscientific fact? To read M. LeRoy one would believe that it is between\nthe first and the second stage, but who does not see that there is a\ngreater distance from the second to the third, and still more from the\nthird to the fourth.\n\nAllow me to cite two examples which perhaps will enlighten us a little.\n\nI observe the deviation of a galvanometer by the aid of a movable mirror\nwhich projects a luminous image or spot on a divided scale. The crude\nfact is this: I see the spot displace itself on the scale, and the\nscientific fact is this: a current passes in the circuit.\n\nOr again: when I make an experiment I should subject the result to\ncertain corrections, because I know I must have made errors. These\nerrors are of two kinds, some are accidental and these I shall correct\nby taking the mean; the others are systematic and I shall be able to\ncorrect those only by a thorough study of their causes. The first result\nobtained is then the fact in the rough, while the scientific fact is the\nfinal result after the finished corrections.\n\nReflecting on this latter example, we are led to subdivide our second\nstage, and in place of saying:\n\n2. The eclipse happened at nine o'clock, we shall say:\n\n2_a_. The eclipse happened when my clock pointed to nine, and\n\n2_b_. My clock being ten minutes slow, the eclipse happened at ten\nminutes past nine.\n\nAnd this is not all: the first stage also should be subdivided, and not\nbetween these two subdivisions will be the least distance; it is\nnecessary to distinguish between the impression of obscurity felt by one\nwitnessing an eclipse, and the affirmation: It grows dark, which this\nimpression extorts from him. In a sense it is the first which is the\nonly true fact in the rough, and the second is already a sort of\nscientific fact.\n\nNow then our scale has six stages, and even though there is no reason\nfor halting at this figure, there we shall stop.\n\nWhat strikes me at the start is this. At the first of our six stages,\nthe fact, still completely in the rough, is, so to speak, individual, it\nis completely distinct from all other possible facts. From the second\nstage, already it is no longer the same. The enunciation of the fact\nwould suit an infinity of other facts. So soon as language intervenes, I\nhave at my command only a finite number of terms to express the shades,\nin number infinite, that my impressions might cover. When I say: It\ngrows dark, that well expresses the impressions I feel in being present\nat an eclipse; but even in obscurity a multitude of shades could be\nimagined, and if, instead of that actually realized, had happened a\nslightly different shade, yet I should still have enunciated this\n_other_ fact by saying: It grows dark.\n\nSecond remark: even at the second stage, the enunciation of a fact can\nonly be _true or false_. This is not so of any proposition; if this\nproposition is the enunciation of a convention, it can not be said that\nthis enunciation is _true_, in the proper sense of the word, since it\ncould not be true apart from me and is true only because I wish it to\nbe.\n\nWhen, for instance, I say the unit for length is the meter, this is a\ndecree that I promulgate, it is not something ascertained which forces\nitself upon me. It is the same, as I think I have elsewhere shown, when\nit is a question, for example, of Euclid's postulate.\n\nWhen I am asked: Is it growing dark? I always know whether I ought to\nreply yes or no. Although an infinity of possible facts may be\nsusceptible of this same enunciation, it grows dark, I shall always\nknow whether the fact realized belongs or does not belong among those\nwhich answer to this enunciation. Facts are classed in categories, and\nif I am asked whether the fact that I ascertain belongs or does not\nbelong in such a category, I shall not hesitate.\n\nDoubtless this classification is sufficiently arbitrary to leave a large\npart to man's freedom or caprice. In a word, this classification is a\nconvention. _This convention being given_, if I am asked: Is such a fact\ntrue? I shall always know what to answer, and my reply will be imposed\nupon me by the witness of my senses.\n\nIf therefore, during an eclipse, it is asked: Is it growing dark? all\nthe world will answer yes. Doubtless those speaking a language where\nbright was called dark, and dark bright, would answer no. But of what\nimportance is that?\n\nIn the same way, in mathematics, _when I have laid down the definitions,\nand the postulates which are conventions_, a theorem henceforth can only\nbe true or false. But to answer the question: Is this theorem true? it\nis no longer to the witness of my senses that I shall have recourse, but\nto reasoning.\n\nA statement of fact is always verifiable, and for the verification we\nhave recourse either to the witness of our senses, or to the memory of\nthis witness. This is properly what characterizes a fact. If you put the\nquestion to me: Is such a fact true? I shall begin by asking you, if\nthere is occasion, to state precisely the conventions, by asking you, in\nother words, what language you have spoken; then once settled on this\npoint, I shall interrogate my senses and shall answer yes or no. But it\nwill be my senses that will have made answer, it will not be _you_ when\nyou say to me: I have spoken to you in English or in French.\n\nIs there something to change in all that when we pass to the following\nstages? When I observe a galvanometer, as I have just said, if I ask an\nignorant visitor: Is the current passing? he looks at the wire to try to\nsee something pass; but if I put the same question to my assistant who\nunderstands my language, he will know I mean: Does the spot move? and he\nwill look at the scale.\n\nWhat difference is there then between the statement of a fact in the\nrough and the statement of a scientific fact? The same difference as\nbetween the statement of the same crude fact in French and in German.\nThe scientific statement is the translation of the crude statement into\na language which is distinguished above all from the common German or\nFrench, because it is spoken by a very much smaller number of people.\n\nYet let us not go too fast. To measure a current I may use a very great\nnumber of types of galvanometers or besides an electrodynamometer. And\nthen when I shall say there is running in this circuit a current of so\nmany amperes, that will mean: if I adapt to this circuit such a\ngalvanometer I shall see the spot come to the division _a_;\nbut that will mean equally: if I adapt to this circuit such an\nelectrodynamometer, I shall see the spot go to the division _b_. And\nthat will mean still many other things, because the current can manifest\nitself not only by mechanical effects, but by effects chemical, thermal,\nluminous, etc.\n\nHere then is one same statement which suits a very great number of facts\nabsolutely different. Why? It is because I assume a law according to\nwhich, whenever such a mechanical effect shall happen, such a chemical\neffect will happen also. Previous experiments, very numerous, have never\nshown this law to fail, and then I have understood that I could express\nby the same statement two facts so invariably bound one to the other.\n\nWhen I am asked: Is the current passing? I can understand that that\nmeans: Will such a mechanical effect happen? But I can understand also:\nWill such a chemical effect happen? I shall then verify either the\nexistence of the mechanical effect, or that of the chemical effect; that\nwill be indifferent, since in both cases the answer must be the same.\n\nAnd if the law should one day be found false? If it was perceived that\nthe concordance of the two effects, mechanical and chemical, is not\nconstant? That day it would be necessary to change the scientific\nlanguage to free it from a grave ambiguity.\n\nAnd after that? Is it thought that ordinary language by aid of which are\nexpressed the facts of daily life is exempt from ambiguity?\n\n_Shall we thence conclude that the facts of daily life are the work of\nthe grammarians?_\n\nYou ask me: Is there a current? I try whether the mechanical effect\nexists, I ascertain it and I answer: Yes, there is a current. You\nunderstand at once that that means that the mechanical effect exists,\nand that the chemical effect, that I have not investigated, exists\nlikewise. Imagine now, supposing an impossibility, the law we believe\ntrue, not to be, and the chemical effect not to exist. Under this\nhypothesis there will be two distinct facts, the one directly observed\nand which is true, the other inferred and which is false. It may\nstrictly be said that we have created the second. So that error is the\npart of man's personal collaboration in the creation of the scientific\nfact.\n\nBut if we can say that the fact in question is false, is this not just\nbecause it is not a free and arbitrary creation of our mind, a disguised\nconvention, in which case it would be neither true nor false. And in\nfact it was verifiable; I had not made the verification, but I could\nhave made it. If I answered amiss, it was because I chose to reply too\nquickly, without having asked nature, who alone knew the secret.\n\nWhen, after an experiment, I correct the accidental and systematic\nerrors to bring out the scientific fact, the case is the same; the\nscientific fact will never be anything but the crude fact translated\ninto another language. When I shall say: It is such an hour, that will\nbe a short way of saying: There is such a relation between the hour\nindicated by my clock, and the hour it marked at the moment of the\npassing of such a star and such another star across the meridian. And\nthis convention of language once adopted, when I shall be asked: Is it\nsuch an hour? it will not depend upon me to answer yes or no.\n\nLet us pass to the stage before the last: the eclipse happened at the\nhour given by the tables deduced from Newton's laws. This is still a\nconvention of language which is perfectly clear for those who know\ncelestial mechanics or simply for those who have the tables calculated\nby the astronomers. I am asked: Did the eclipse happen at the hour\npredicted? I look in the nautical almanac, I see that the eclipse was\nannounced for nine o'clock and I understand that the question means: Did\nthe eclipse happen at nine o'clock? There still we have nothing to\nchange in our conclusions. _The scientific fact is only the crude fact\ntranslated into a convenient language._\n\nIt is true that at the last stage things change. Does the earth rotate?\nIs this a verifiable fact? Could Galileo and the Grand Inquisitor, to\nsettle the matter, appeal to the witness of their senses? On the\ncontrary, they were in accord about the appearances, and whatever had\nbeen the accumulated experiences, they would have remained in accord\nwith regard to the appearances without ever agreeing on their\ninterpretation. It is just on that account that they were obliged to\nhave recourse to procedures of discussion so unscientific.\n\nThis is why I think they did not disagree about a _fact_: we have not\nthe right to give the same name to the rotation of the earth, which was\nthe object of their discussion, and to the facts crude or scientific we\nhave hitherto passed in review.\n\nAfter what precedes, it seems superfluous to investigate whether the\nfact in the rough is outside of science, because there can neither be\nscience without scientific fact, nor scientific fact without fact in the\nrough, since the first is only the translation of the second.\n\nAnd then, has one the right to say that the scientist creates the\nscientific fact? First of all, he does not create it from nothing, since\nhe makes it with the fact in the rough. Consequently he does not make it\nfreely and _as he chooses_. However able the worker may be, his freedom\nis always limited by the properties of the raw material on which he\nworks.\n\nAfter all, what do you mean when you speak of this free creation of the\nscientific fact and when you take as example the astronomer who\nintervenes actively in the phenomenon of the eclipse by bringing his\nclock? Do you mean: The eclipse happened at nine o'clock; but if the\nastronomer had wished it to happen at ten, that depended only on him, he\nhad only to advance his clock an hour?\n\nBut the astronomer, in perpetrating that bad joke, would evidently have\nbeen guilty of an equivocation. When he tells me: The eclipse happened\nat nine, I understand that nine is the hour deduced from the crude\nindication of the pendulum by the usual series of corrections. If he has\ngiven me solely that crude indication, or if he has made corrections\ncontrary to the habitual rules, he has changed the language agreed upon\nwithout forewarning me. If, on the contrary, he took care to forewarn\nme, I have nothing to complain of, but then it is always the same fact\nexpressed in another language.\n\nIn sum, _all the scientist creates in a fact is the language in which he\nenunciates it_. If he predicts a fact, he will employ this language, and\nfor all those who can speak and understand it, his prediction is free\nfrom ambiguity. Moreover, this prediction once made, it evidently does\nnot depend upon him whether it is fulfilled or not.\n\nWhat then remains of M. LeRoy's thesis? This remains: the scientist\nintervenes actively in choosing the facts worth observing. An isolated\nfact has by itself no interest; it becomes interesting if one has reason\nto think that it may aid in the prediction of other facts; or better,\nif, having been predicted, its verification is the confirmation of a\nlaw. Who shall choose the facts which, corresponding to these\nconditions, are worthy the freedom of the city in science? This is the\nfree activity of the scientist.\n\nAnd that is not all. I have said that the scientific fact is the\ntranslation of a crude fact into a certain language; I should add that\nevery scientific fact is formed of many crude facts. This is\nsufficiently shown by the examples cited above. For instance, for the\nhour of the eclipse my clock marked the hour [alpha] at the instant of\nthe eclipse; it marked the hour [beta] at the moment of the last transit\nof the meridian of a certain star that we take as origin of right\nascensions; it marked the hour [gamma] at the moment of the preceding\ntransit of this same star. There are three distinct facts (still it will\nbe noticed that each of them results itself from two simultaneous facts\nin the rough; but let us pass this over). In place of that I say: The\neclipse happened at the hour 24 ([alpha]-[beta])/([beta]-[gamma]), and\nthe three facts are combined in a single scientific fact. I have\nconcluded that the three readings, [alpha], [beta], [gamma] made on my\nclock at three different moments lacked interest and that the only thing\ninteresting was the combination ([alpha]-[beta])/([beta]-[gamma]) of\nthe three. In this conclusion is found the free activity of my mind.\n\nBut I have thus used up my power; I can not make this combination\n([alpha]-[beta])/([beta]-[gamma]) have such a value and not such\nanother, since I can not influence either the value of [alpha], or that\nof [beta], or that of [gamma], which are imposed upon me as crude\nfacts.\n\nIn sum, facts are facts, and _if it happens that they satisfy a\nprediction, this is not an effect of our free activity_. There is no\nprecise frontier between the fact in the rough and the scientific fact;\nit can only be said that such an enunciation of fact is _more crude_ or,\non the contrary, _more scientific_ than such another.\n\n\n4. _'Nominalism' and 'the Universal Invariant'_\n\nIf from facts we pass to laws, it is clear that the part of the free\nactivity of the scientist will become much greater. But did not M. LeRoy\nmake it still too great? This is what we are about to examine.\n\nRecall first the examples he has given. When I say: Phosphorus melts at\n44\u00b0, I think I am enunciating a law; in reality it is just the\ndefinition of phosphorus; if one should discover a body which,\npossessing otherwise all the properties of phosphorus, did not melt at\n44\u00b0, we should give it another name, that is all, and the law would\nremain true.\n\nJust so when I say: Heavy bodies falling freely pass over spaces\nproportional to the squares of the times, I only give the definition of\nfree fall. Whenever the condition shall not be fulfilled, I shall say\nthat the fall is not free, so that the law will never be wrong. It is\nclear that if laws were reduced to that, they could not serve in\nprediction; then they would be good for nothing, either as means of\nknowledge or as principle of action.\n\nWhen I say: Phosphorus melts at 44\u00b0, I mean by that: All bodies\npossessing such or such a property (to wit, all the properties of\nphosphorus, save fusing-point) fuse at 44\u00b0. So understood, my\nproposition is indeed a law, and this law may be useful to me, because\nif I meet a body possessing these properties I shall be able to predict\nthat it will fuse at 44\u00b0.\n\nDoubtless the law may be found to be false. Then we shall read in the\ntreatises on chemistry: \"There are two bodies which chemists long\nconfounded under the name of phosphorus; these two bodies differ only by\ntheir points of fusion.\" That would evidently not be the first time for\nchemists to attain to the separation of two bodies they were at first\nnot able to distinguish; such, for example, are neodymium and\npraseodymium, long confounded under the name of didymium.\n\nI do not think the chemists much fear that a like mischance will ever\nhappen to phosphorus. And if, to suppose the impossible, it should\nhappen, the two bodies would probably not have _identically_ the same\ndensity, _identically_ the same specific heat, etc., so that after\nhaving determined with care the density, for instance, one could still\nforesee the fusion point.\n\nIt is, moreover, unimportant; it suffices to remark that there is a law,\nand that this law, true or false, does not reduce to a tautology.\n\nWill it be said that if we do not know on the earth a body which does\nnot fuse at 44\u00b0 while having all the other properties of phosphorus, we\ncan not know whether it does not exist on other planets? Doubtless that\nmay be maintained, and it would then be inferred that the law in\nquestion, which may serve as a rule of action to us who inhabit the\nearth, has yet no general value from the point of view of knowledge, and\nowes its interest only to the chance which has placed us on this globe.\nThis is possible, but, if it were so, the law would be valueless, not\nbecause it reduced to a convention, but because it would be false.\n\nThe same is true in what concerns the fall of bodies. It would do me no\ngood to have given the name of free fall to falls which happen in\nconformity with Galileo's law, if I did not know that elsewhere, in such\ncircumstances, the fall will be _probably_ free or _approximately_ free.\nThat then is a law which may be true or false, but which does not reduce\nto a convention.\n\nSuppose the astronomers discover that the stars do not exactly obey\nNewton's law. They will have the choice between two attitudes; they may\nsay that gravitation does not vary exactly as the inverse of the square\nof the distance, or else they may say that gravitation is not the only\nforce which acts on the stars and that there is in addition a different\nsort of force.\n\nIn the second case, Newton's law will be considered as the definition of\ngravitation. This will be the nominalist attitude. The choice between\nthe two attitudes is free, and is made from considerations of\nconvenience, though these considerations are most often so strong that\nthere remains practically little of this freedom.\n\nWe can break up this proposition: (1) The stars obey Newton's law, into\ntwo others; (2) gravitation obeys Newton's law; (3) gravitation is the\nonly force acting on the stars. In this case proposition (2) is no\nlonger anything but a definition and is beyond the test of experiment;\nbut then it will be on proposition (3) that this check can be exercised.\nThis is indeed necessary, since the resulting proposition (1) predicts\nverifiable facts in the rough.\n\nIt is thanks to these artifices that by an unconscious nominalism the\nscientists have elevated above the laws what they call principles. When\na law has received a sufficient confirmation from experiment, we may\nadopt two attitudes: either we may leave this law in the fray; it will\nthen remain subjected to an incessant revision, which without any doubt\nwill end by demonstrating that it is only approximative. Or else we may\nelevate it into a _principle_ by adopting conventions such that the\nproposition may be certainly true. For that the procedure is always the\nsame. The primitive law enunciated a relation between two facts in the\nrough, _A_ and _B_; between these two crude facts is introduced an\nabstract intermediary _C_, more or less fictitious (such was in the\npreceding example the impalpable entity, gravitation). And then we have\na relation between _A_ and _C_ that we may suppose rigorous and which is\nthe _principle_; and another between _C_ and _B_ which remains a _law_\nsubject to revision.\n\nThe principle, henceforth crystallized, so to speak, is no longer\nsubject to the test of experiment. It is not true or false, it is\nconvenient.\n\nGreat advantages have often been found in proceeding in that way, but it\nis clear that if _all_ the laws had been transformed into principles\n_nothing_ would be left of science. Every law may be broken up into a\nprinciple and a law, but thereby it is very clear that, however far this\npartition be pushed, there will always remain laws.\n\nNominalism has therefore limits, and this is what one might fail to\nrecognize if one took to the very letter M. LeRoy's assertions.\n\nA rapid review of the sciences will make us comprehend better what are\nthese limits. The nominalist attitude is justified only when it is\nconvenient; when is it so?\n\nExperiment teaches us relations between bodies; this is the fact in the\nrough; these relations are extremely complicated. Instead of envisaging\ndirectly the relation of the body _A_ and the body _B_, we introduce\nbetween them an intermediary, which is space, and we envisage three\ndistinct relations: that of the body _A_ with the figure _A'_ of space,\nthat of the body _B_ with the figure _B'_ of space, that of the two\nfigures _A'_ and _B'_ to each other. Why is this detour advantageous?\nBecause the relation of _A_ and _B_ was complicated, but differed little\nfrom that of _A'_ and _B'_, which is simple; so that this complicated\nrelation may be replaced by the simple relation between _A'_ and _B'_\nand by two other relations which tell us that the differences between\n_A_ and _A'_, on the one hand, between _B_ and _B'_, on the other hand,\nare _very small_. For example, if _A_ and _B_ are two natural solid\nbodies which are displaced with slight deformation, we envisage two\nmovable _rigid_ figures _A'_ and _B'_. The laws of the relative\ndisplacement of these figures _A'_ and _B'_ will be very simple; they\nwill be those of geometry. And we shall afterward add that the body _A_,\nwhich always differs very little from _A'_, dilates from the effect of\nheat and bends from the effect of elasticity. These dilatations and\nflexions, just because they are very small, will be for our mind\nrelatively easy to study. Just imagine to what complexities of language\nit would have been necessary to be resigned if we had wished to\ncomprehend in the same enunciation the displacement of the solid, its\ndilatation and its flexure?\n\nThe relation between _A_ and _B_ was a rough law, and was broken up; we\nnow have two laws which express the relations of _A_ and _A'_, of _B_\nand _B'_, and a principle which expresses that of _A'_ with _B'_. It is\nthe aggregate of these principles that is called geometry.\n\nTwo other remarks. We have a relation between two bodies _A_ and _B_,\nwhich we have replaced by a relation between two figures _A'_ and _B'_;\nbut this same relation between the same two figures _A'_ and _B'_ could\njust as well have replaced advantageously a relation between two other\nbodies _A''_ and _B''_, entirely different from _A_ and _B_. And that in\nmany ways. If the principles of geometry had not been invented, after\nhaving studied the relation of _A_ and _B_, it would be necessary to\nbegin again _ab ovo_ the study of the relation of _A''_ and _B''_.\nThat is why geometry is so precious. A geometrical relation can\nadvantageously replace a relation which, considered in the rough state,\nshould be regarded as mechanical, it can replace another which should be\nregarded as optical, etc.\n\nYet let no one say: But that proves geometry an experimental science; in\nseparating its principles from laws whence they have been drawn, you\nartificially separate it itself from the sciences which have given birth\nto it. The other sciences have likewise principles, but that does not\npreclude our having to call them experimental.\n\nIt must be recognized that it would have been difficult not to make this\nseparation that is pretended to be artificial. We know the r\u00f4le that the\nkinematics of solid bodies has played in the genesis of geometry; should\nit then be said that geometry is only a branch of experimental\nkinematics? But the laws of the rectilinear propagation of light have\nalso contributed to the formation of its principles. Must geometry be\nregarded both as a branch of kinematics and as a branch of optics? I\nrecall besides that our Euclidean space which is the proper object of\ngeometry has been chosen, for reasons of convenience, from among a\ncertain number of types which preexist in our mind and which are called\ngroups.\n\nIf we pass to mechanics, we still see great principles whose origin is\nanalogous, and, as their 'radius of action,' so to speak, is smaller,\nthere is no longer reason to separate them from mechanics proper and to\nregard this science as deductive.\n\nIn physics, finally, the r\u00f4le of the principles is still more\ndiminished. And in fact they are only introduced when it is of\nadvantage. Now they are advantageous precisely because they are few,\nsince each of them very nearly replaces a great number of laws.\nTherefore it is not of interest to multiply them. Besides an outcome is\nnecessary, and for that it is needful to end by leaving abstraction to\ntake hold of reality.\n\nSuch are the limits of nominalism, and they are narrow.\n\nM. LeRoy has insisted, however, and he has put the question under\nanother form.\n\nSince the enunciation of our laws may vary with the conventions that we\nadopt, since these conventions may modify even the natural relations of\nthese laws, is there in the manifold of these laws something independent\nof these conventions and which may, so to speak, play the r\u00f4le of\n_universal invariant_? For instance, the fiction has been introduced of\nbeings who, having been educated in a world different from ours, would\nhave been led to create a non-Euclidean geometry. If these beings were\nafterward suddenly transported into our world, they would observe the\nsame laws as we, but they would enunciate them in an entirely different\nway. In truth there would still be something in common between the two\nenunciations, but this is because these beings do not yet differ enough\nfrom us. Beings still more strange may be imagined, and the part common\nto the two systems of enunciations will shrink more and more. Will it\nthus shrink in convergence toward zero, or will there remain an\nirreducible residue which will then be the universal invariant sought?\n\nThe question calls for precise statement. Is it desired that this common\npart of the enunciations be expressible in words? It is clear, then,\nthat there are not words common to all languages, and we can not pretend\nto construct I know not what universal invariant which should be\nunderstood both by us and by the fictitious non-Euclidean geometers of\nwhom I have just spoken; no more than we can construct a phrase which\ncan be understood both by Germans who do not understand French and by\nFrench who do not understand German. But we have fixed rules which\npermit us to translate the French enunciations into German, and\ninversely. It is for that that grammars and dictionaries have been made.\nThere are also fixed rules for translating the Euclidean language into\nthe non-Euclidean language, or, if there are not, they could be made.\n\nAnd even if there were neither interpreter nor dictionary, if the\nGermans and the French, after having lived centuries in separate worlds,\nfound themselves all at once in contact, do you think there would be\nnothing in common between the science of the German books and that of\nthe French books? The French and the Germans would certainly end by\nunderstanding each other, as the American Indians ended by understanding\nthe language of their conquerors after the arrival of the Spanish.\n\nBut, it will be said, doubtless the French would be capable of\nunderstanding the Germans even without having learned German, but this\nis because there remains between the French and the Germans something in\ncommon, since both are men. We should still attain to an understanding\nwith our hypothetical non-Euclideans, though they be not men, because\nthey would still retain something human. But in any case a minimum of\nhumanity is necessary.\n\nThis is possible, but I shall observe first that this little humanness\nwhich would remain in the non-Euclideans would suffice not only to make\npossible the translation of _a little_ of their language, but to make\npossible the translation of _all_ their language.\n\nNow, that there must be a minimum is what I concede; suppose there\nexists I know not what fluid which penetrates between the molecules of\nour matter, without having any action on it and without being subject to\nany action coming from it. Suppose beings sensible to the influence of\nthis fluid and insensible to that of our matter. It is clear that the\nscience of these beings would differ absolutely from ours and that it\nwould be idle to seek an 'invariant' common to these two sciences. Or\nagain, if these beings rejected our logic and did not admit, for\ninstance, the principle of contradiction.\n\nBut truly I think it without interest to examine such hypotheses.\n\nAnd then, if we do not push whimsicality so far, if we introduce only\nfictitious beings having senses analogous to ours and sensible to the\nsame impressions, and moreover admitting the principles of our logic, we\nshall then be able to conclude that their language, however different\nfrom ours it may be, would always be capable of translation. Now the\npossibility of translation implies the existence of an invariant. To\ntranslate is precisely to disengage this invariant. Thus, to decipher a\ncryptogram is to seek what in this document remains invariant, when the\nletters are permuted.\n\nWhat now is the nature of this invariant it is easy to understand, and a\nword will suffice us. The invariant laws are the relations between the\ncrude facts, while the relations between the 'scientific facts' remain\nalways dependent on certain conventions.\n\n\n\n\nCHAPTER XI\n\nSCIENCE AND REALITY\n\n\n5. _Contingence and Determinism_\n\nI do not intend to treat here the question of the contingence of the\nlaws of nature, which is evidently insoluble, and on which so much has\nalready been written. I only wish to call attention to what different\nmeanings have been given to this word, contingence, and how advantageous\nit would be to distinguish them.\n\nIf we look at any particular law, we may be certain in advance that it\ncan only be approximate. It is, in fact, deduced from experimental\nverifications, and these verifications were and could be only\napproximate. We should always expect that more precise measurements will\noblige us to add new terms to our formulas; this is what has happened,\nfor instance, in the case of Mariotte's law.\n\nMoreover the statement of any law is necessarily incomplete. This\nenunciation should comprise the enumeration of _all_ the antecedents in\nvirtue of which a given consequent can happen. I should first describe\n_all_ the conditions of the experiment to be made and the law would then\nbe stated: If all the conditions are fulfilled, the phenomenon will\nhappen.\n\nBut we shall be sure of not having forgotten _any_ of these conditions\nonly when we shall have described the state of the entire universe at\nthe instant _t_; all the parts of this universe may, in fact, exercise\nan influence more or less great on the phenomenon which must happen at\nthe instant _t_ + _dt_.\n\nNow it is clear that such a description could not be found in the\nenunciation of the law; besides, if it were made, the law would become\nincapable of application; if one required so many conditions, there\nwould be very little chance of their ever being all realized at any\nmoment.\n\nThen as one can never be certain of not having forgotten some essential\ncondition, it can not be said: If such and such conditions are\nrealized, such a phenomenon will occur; it can only be said: If such and\nsuch conditions are realized, it is probable that such a phenomenon will\noccur, very nearly.\n\nTake the law of gravitation, which is the least imperfect of all known\nlaws. It enables us to foresee the motions of the planets. When I use\nit, for instance, to calculate the orbit of Saturn, I neglect the action\nof the stars, and in doing so I am certain of not deceiving myself,\nbecause I know that these stars are too far away for their action to be\nsensible.\n\nI announce, then, with a quasi-certitude that the coordinates of Saturn\nat such an hour will be comprised between such and such limits. Yet is\nthat certitude absolute? Could there not exist in the universe some\ngigantic mass, much greater than that of all the known stars and whose\naction could make itself felt at great distances? That mass might be\nanimated by a colossal velocity, and after having circulated from all\ntime at such distances that its influence had remained hitherto\ninsensible to us, it might come all at once to pass near us. Surely it\nwould produce in our solar system enormous perturbations that we could\nnot have foreseen. All that can be said is that such an event is wholly\nimprobable, and then, instead of saying: Saturn will be near such a\npoint of the heavens, we must limit ourselves to saying: Saturn will\nprobably be near such a point of the heavens. Although this probability\nmay be practically equivalent to certainty, it is only a probability.\n\nFor all these reasons, no particular law will ever be more than\napproximate and probable. Scientists have never failed to recognize this\ntruth; only they believe, right or wrong, that every law may be replaced\nby another closer and more probable, that this new law will itself be\nonly provisional, but that the same movement can continue indefinitely,\nso that science in progressing will possess laws more and more probable,\nthat the approximation will end by differing as little as you choose\nfrom exactitude and the probability from certitude.\n\nIf the scientists who think thus are right, still could it be said that\n_the_ laws of nature are contingent, even though _each_ law, taken in\nparticular, may be qualified as contingent? Or must one require, before\nconcluding the contingence _of the_ natural laws, that this progress\nhave an end, that the scientist finish some day by being arrested in his\nsearch for a closer and closer approximation, and that, beyond a certain\nlimit, he thereafter meet in nature only caprice?\n\nIn the conception of which I have just spoken (and which I shall call\nthe scientific conception), every law is only a statement imperfect and\nprovisional, but it must one day be replaced by another, a superior law,\nof which it is only a crude image. No place therefore remains for the\nintervention of a free will.\n\nIt seems to me that the kinetic theory of gases will furnish us a\nstriking example.\n\nYou know that in this theory all the properties of gases are explained\nby a simple hypothesis; it is supposed that all the gaseous molecules\nmove in every direction with great velocities and that they follow\nrectilineal paths which are disturbed only when one molecule passes very\nnear the sides of the vessel or another molecule. The effects our crude\nsenses enable us to observe are the mean effects, and in these means,\nthe great deviations compensate, or at least it is very improbable that\nthey do not compensate; so that the observable phenomena follow simple\nlaws such as that of Mariotte or of Gay-Lussac. But this compensation of\ndeviations is only probable. The molecules incessantly change place and\nin these continual displacements the figures they form pass successively\nthrough all possible combinations. Singly these combinations are very\nnumerous; almost all are in conformity with Mariotte's law, only a few\ndeviate from it. These also will happen, only it would be necessary to\nwait a long time for them. If a gas were observed during a sufficiently\nlong time it would certainly be finally seen to deviate, for a very\nshort time, from Mariotte's law. How long would it be necessary to wait?\nIf it were desired to calculate the probable number of years, it would\nbe found that this number is so great that to write only the number of\nplaces of figures employed would still require half a score places of\nfigures. No matter; enough that it may be done.\n\nI do not care to discuss here the value of this theory. It is evident\nthat if it be adopted, Mariotte's law will thereafter appear only as\ncontingent, since a day will come when it will not be true. And yet,\nthink you the partisans of the kinetic theory are adversaries of\ndeterminism? Far from it; they are the most ultra of mechanists. Their\nmolecules follow rigid paths, from which they depart only under the\ninfluence of forces which vary with the distance, following a perfectly\ndeterminate law. There remains in their system not the smallest place\neither for freedom, or for an evolutionary factor, properly so-called,\nor for anything whatever that could be called contingence. I add, to\navoid mistake, that neither is there any evolution of Mariotte's law\nitself; it ceases to be true after I know not how many centuries; but at\nthe end of a fraction of a second it again becomes true and that for an\nincalculable number of centuries.\n\nAnd since I have pronounced the word evolution, let us clear away\nanother mistake. It is often said: Who knows whether the laws do not\nevolve and whether we shall not one day discover that they were not at\nthe Carboniferous epoch what they are to-day? What are we to understand\nby that? What we think we know about the past state of our globe, we\ndeduce from its present state. And how is this deduction made? It is by\nmeans of laws supposed known. The law, being a relation between the\nantecedent and the consequent, enables us equally well to deduce the\nconsequent from the antecedent, that is, to foresee the future, and to\ndeduce the antecedent from the consequent, that is, to conclude from the\npresent to the past. The astronomer who knows the present situation of\nthe stars can from it deduce their future situation by Newton's law, and\nthis is what he does when he constructs ephemerides; and he can equally\ndeduce from it their past situation. The calculations he thus can make\ncan not teach him that Newton's law will cease to be true in the future,\nsince this law is precisely his point of departure; not more can they\ntell him it was not true in the past. Still, in what concerns the\nfuture, his ephemerides can one day be tested and our descendants will\nperhaps recognize that they were false. But in what concerns the past,\nthe geologic past which had no witnesses, the results of his\ncalculation, like those of all speculations where we seek to deduce the\npast from the present, escape by their very nature every species of\ntest. So that if the laws of nature were not the same in the\nCarboniferous age as at the present epoch, we shall never be able to\nknow it, since we can know nothing of this age, only what we deduce from\nthe hypothesis of the permanence of these laws.\n\nPerhaps it will be said that this hypothesis might lead to contradictory\nresults and that we shall be obliged to abandon it. Thus, in what\nconcerns the origin of life, we may conclude that there have always been\nliving beings, since the present world shows us always life springing\nfrom life; and we may also conclude that there have not always been,\nsince the application of the existent laws of physics to the present\nstate of our globe teaches us that there was a time when this globe was\nso warm that life on it was impossible. But contradictions of this sort\ncan always be removed in two ways; it may be supposed that the actual\nlaws of nature are not exactly what we have assumed; or else it may be\nsupposed that the laws of nature actually are what we have assumed, but\nthat it has not always been so.\n\nIt is evident that the actual laws will never be sufficiently well known\nfor us not to be able to adopt the first of these two solutions and for\nus to be constrained to infer the evolution of natural laws.\n\nOn the other hand, suppose such an evolution; assume, if you wish, that\nhumanity lasts sufficiently long for this evolution to have witnesses.\nThe _same_ antecedent shall produce, for instance, different consequents\nat the Carboniferous epoch and at the Quaternary. That evidently means\nthat the antecedents are closely alike; if all the circumstances were\nidentical, the Carboniferous epoch would be indistinguishable from the\nQuaternary. Evidently this is not what is supposed. What remains is that\nsuch antecedent, accompanied by such accessory circumstance, produces\nsuch consequent; and that the same antecedent, accompanied by such other\naccessory circumstance, produces such other consequent. Time does not\nenter into the affair.\n\nThe law, such as ill-informed science would have stated it, and which\nwould have affirmed that this antecedent always produces this\nconsequent, without taking account of the accessory circumstances, this\nlaw, which was only approximate and probable, must be replaced by\nanother law more approximate and more probable, which brings in these\naccessory circumstances. We always come back, therefore, to that same\nprocess which we have analyzed above, and if humanity should discover\nsomething of this sort, it would not say that it is the laws which have\nevoluted, but the circumstances which have changed.\n\nHere, therefore, are several different senses of the word contingence.\nM. LeRoy retains them all and he does not sufficiently distinguish them,\nbut he introduces a new one. Experimental laws are only approximate, and\nif some appear to us as exact, it is because we have artificially\ntransformed them into what I have above called a principle. We have made\nthis transformation freely, and as the caprice which has determined us\nto make it is something eminently contingent, we have communicated this\ncontingence to the law itself. It is in this sense that we have the\nright to say that determinism supposes freedom, since it is freely that\nwe become determinists. Perhaps it will be found that this is to give\nlarge scope to nominalism and that the introduction of this new sense of\nthe word contingence will not help much to solve all those questions\nwhich naturally arise and of which we have just been speaking.\n\nI do not at all wish to investigate here the foundations of the\nprinciple of induction; I know very well that I should not succeed; it\nis as difficult to justify this principle as to get on without it. I\nonly wish to show how scientists apply it and are forced to apply it.\n\nWhen the same antecedent recurs, the same consequent must likewise\nrecur; such is the ordinary statement. But reduced to these terms this\nprinciple could be of no use. For one to be able to say that the same\nantecedent recurred, it would be necessary for the circumstances _all_\nto be reproduced, since no one is absolutely indifferent, and for them\nto be _exactly_ reproduced. And, as that will never happen, the\nprinciple can have no application.\n\nWe should therefore modify the enunciation and say: If an antecedent _A_\nhas once produced a consequent _B_, an antecedent _A'_, slightly\ndifferent from _A_, will produce a consequent _B'_, slightly different\nfrom _B_. But how shall we recognize that the antecedents _A_ and _A'_\nare 'slightly different'? If some one of the circumstances can be\nexpressed by a number, and this number has in the two cases values very\nnear together, the sense of the phrase 'slightly different' is\nrelatively clear; the principle then signifies that the consequent is a\ncontinuous function of the antecedent. And as a practical rule, we reach\nthis conclusion that we have the right to interpolate. This is in fact\nwhat scientists do every day, and without interpolation all science\nwould be impossible.\n\nYet observe one thing. The law sought may be represented by a curve.\nExperiment has taught us certain points of this curve. In virtue of the\nprinciple we have just stated, we believe these points may be connected\nby a continuous graph. We trace this graph with the eye. New experiments\nwill furnish us new points of the curve. If these points are outside of\nthe graph traced in advance, we shall have to modify our curve, but not\nto abandon our principle. Through any points, however numerous they may\nbe, a continuous curve may always be passed. Doubtless, if this curve is\ntoo capricious, we shall be shocked (and we shall even suspect errors of\nexperiment), but the principle will not be directly put at fault.\n\nFurthermore, among the circumstances of a phenomenon, there are some\nthat we regard as negligible, and we shall consider _A_ and _A'_ as\nslightly different if they differ only by these accessory circumstances.\nFor instance, I have ascertained that hydrogen unites with oxygen under\nthe influence of the electric spark, and I am certain that these two\ngases will unite anew, although the longitude of Jupiter may have\nchanged considerably in the interval. We assume, for instance, that the\nstate of distant bodies can have no sensible influence on terrestrial\nphenomena, and that seems in fact requisite, but there are cases where\nthe choice of these practically indifferent circumstances admits of more\narbitrariness or, if you choose, requires more tact.\n\nOne more remark: The principle of induction would be inapplicable if\nthere did not exist in nature a great quantity of bodies like one\nanother, or almost alike, and if we could not infer, for instance, from\none bit of phosphorus to another bit of phosphorus.\n\nIf we reflect on these considerations, the problem of determinism and of\ncontingence will appear to us in a new light.\n\nSuppose we were able to embrace the series of all phenomena of the\nuniverse in the whole sequence of time. We could envisage what might be\ncalled the _sequences_; I mean relations between antecedent and\nconsequent. I do not wish to speak of constant relations or laws, I\nenvisage separately (individually, so to speak) the different sequences\nrealized.\n\nWe should then recognize that among these sequences there are no two\naltogether alike. But, if the principle of induction, as we have just\nstated it, is true, there will be those almost alike and that can be\nclassed alongside one another. In other words, it is possible to make a\nclassification of sequences.\n\nIt is to the possibility and the legitimacy of such a classification\nthat determinism, in the end, reduces. This is all that the preceding\nanalysis leaves of it. Perhaps under this modest form it will seem less\nappalling to the moralist.\n\nIt will doubtless be said that this is to come back by a detour to M.\nLeRoy's conclusion which a moment ago we seemed to reject: we are\ndeterminists voluntarily. And in fact all classification supposes the\nactive intervention of the classifier. I agree that this may be\nmaintained, but it seems to me that this detour will not have been\nuseless and will have contributed to enlighten us a little.\n\n\n6. _Objectivity of Science_\n\nI arrive at the question set by the title of this article: What is the\nobjective value of science? And first what should we understand by\nobjectivity?\n\nWhat guarantees the objectivity of the world in which we live is that\nthis world is common to us with other thinking beings. Through the\ncommunications that we have with other men, we receive from them\nready-made reasonings; we know that these reasonings do not come from us\nand at the same time we recognize in them the work of reasonable beings\nlike ourselves. And as these reasonings appear to fit the world of our\nsensations, we think we may infer that these reasonable beings have seen\nthe same thing as we; thus it is we know we have not been dreaming.\n\nSuch, therefore, is the first condition of objectivity; what is\nobjective must be common to many minds and consequently transmissible\nfrom one to the other, and as this transmission can only come about by\nthat 'discourse' which inspires so much distrust in M. LeRoy, we are\neven forced to conclude: no discourse, no objectivity.\n\nThe sensations of others will be for us a world eternally closed. We\nhave no means of verifying that the sensation I call red is the same as\nthat which my neighbor calls red.\n\nSuppose that a cherry and a red poppy produce on me the sensation _A_\nand on him the sensation _B_ and that, on the contrary, a leaf produces\non me the sensation _B_ and on him the sensation _A_. It is clear we\nshall never know anything about it; since I shall call red the sensation\n_A_ and green the sensation _B_, while he will call the first green and\nthe second red. In compensation, what we shall be able to ascertain is\nthat, for him as for me, the cherry and the red poppy produce the _same_\nsensation, since he gives the same name to the sensations he feels and I\ndo the same.\n\nSensations are therefore intransmissible, or rather all that is pure\nquality in them is intransmissible and forever impenetrable. But it is\nnot the same with relations between these sensations.\n\nFrom this point of view, all that is objective is devoid of all quality\nand is only pure relation. Certes, I shall not go so far as to say that\nobjectivity is only pure quantity (this would be to particularize too\nfar the nature of the relations in question), but we understand how some\none could have been carried away into saying that the world is only a\ndifferential equation.\n\nWith due reserve regarding this paradoxical proposition, we must\nnevertheless admit that nothing is objective which is not transmissible,\nand consequently that the relations between the sensations can alone\nhave an objective value.\n\nPerhaps it will be said that the esthetic emotion, which is common to\nall mankind, is proof that the qualities of our sensations are also the\nsame for all men and hence are objective. But if we think about this, we\nshall see that the proof is not complete; what is proved is that this\nemotion is aroused in John as in James by the sensations to which James\nand John give the same name or by the corresponding combinations of\nthese sensations; either because this emotion is associated in John with\nthe sensation _A_, which John calls red, while parallelly it is\nassociated in James with the sensation _B_, which James calls red; or\nbetter because this emotion is aroused, not by the qualities themselves\nof the sensations, but by the harmonious combination of their relations\nof which we undergo the unconscious impression.\n\nSuch a sensation is beautiful, not because it possesses such a quality,\nbut because it occupies such a place in the woof of our associations of\nideas, so that it can not be excited without putting in motion the\n'receiver' which is at the other end of the thread and which corresponds\nto the artistic emotion.\n\nWhether we take the moral, the esthetic or the scientific point of view,\nit is always the same thing. Nothing is objective except what is\nidentical for all; now we can only speak of such an identity if a\ncomparison is possible, and can be translated into a 'money of exchange'\ncapable of transmission from one mind to another. Nothing, therefore,\nwill have objective value except what is transmissible by 'discourse,'\nthat is, intelligible.\n\nBut this is only one side of the question. An absolutely disordered\naggregate could not have objective value since it would be\nunintelligible, but no more can a well-ordered assemblage have it, if it\ndoes not correspond to sensations really experienced. It seems to me\nsuperfluous to recall this condition, and I should not have dreamed of\nit, if it had not lately been maintained that physics is not an\nexperimental science. Although this opinion has no chance of being\nadopted either by physicists or by philosophers, it is well to be warned\nso as not to let oneself slip over the declivity which would lead\nthither. Two conditions are therefore to be fulfilled, and if the first\nseparates reality[11] from the dream, the second distinguishes it from\nthe romance.\n\n [11] I here use the word real as a synonym of objective; I thus\n conform to common usage; perhaps I am wrong, our dreams are\n real, but they are not objective.\n\nNow what is science? I have explained in the preceding article, it is\nbefore all a classification, a manner of bringing together facts which\nappearances separate, though they were bound together by some natural\nand hidden kinship. Science, in other words, is a system of relations.\nNow we have just said, it is in the relations alone that objectivity\nmust be sought; it would be vain to seek it in beings considered as\nisolated from one another.\n\nTo say that science can not have objective value since it teaches us\nonly relations, this is to reason backward, since, precisely, it is\nrelations alone which can be regarded as objective.\n\nExternal objects, for instance, for which the word _object_ was\ninvented, are really _objects_ and not fleeting and fugitive\nappearances, because they are not only groups of sensations, but groups\ncemented by a constant bond. It is this bond, and this bond alone, which\nis the object in itself, and this bond is a relation.\n\nTherefore, when we ask what is the objective value of science, that does\nnot mean: Does science teach us the true nature of things? but it means:\nDoes it teach us the true relations of things?\n\nTo the first question, no one would hesitate to reply, no; but I think\nwe may go farther; not only science can not teach us the nature of\nthings; but nothing is capable of teaching it to us, and if any god knew\nit, he could not find words to express it. Not only can we not divine\nthe response, but if it were given to us we could understand nothing of\nit; I ask myself even whether we really understand the question.\n\nWhen, therefore, a scientific theory pretends to teach us what heat is,\nor what is electricity, or life, it is condemned beforehand; all it can\ngive us is only a crude image. It is, therefore, provisional and\ncrumbling.\n\nThe first question being out of reason, the second remains. Can science\nteach us the true relations of things? What it joins together should\nthat be put asunder, what it puts asunder should that be joined\ntogether?\n\nTo understand the meaning of this new question, it is needful to refer\nto what was said above on the conditions of objectivity. Have these\nrelations an objective value? That means: Are these relations the same\nfor all? Will they still be the same for those who shall come after us?\n\nIt is clear that they are not the same for the scientist and the\nignorant person. But that is unimportant, because if the ignorant person\ndoes not see them all at once, the scientist may succeed in making him\nsee them by a series of experiments and reasonings. The thing essential\nis that there are points on which all those acquainted with the\nexperiments made can reach accord.\n\nThe question is to know whether this accord will be durable and whether\nit will persist for our successors. It may be asked whether the unions\nthat the science of to-day makes will be confirmed by the science of\nto-morrow. To affirm that it will be so we can not invoke any _a priori_\nreason; but this is a question of fact, and science has already lived\nlong enough for us to be able to find out by asking its history whether\nthe edifices it builds stand the test of time, or whether they are only\nephemeral constructions.\n\nNow what do we see? At the first blush, it seems to us that the theories\nlast only a day and that ruins upon ruins accumulate. To-day the\ntheories are born, to-morrow they are the fashion, the day after\nto-morrow they are classic, the fourth day they are superannuated, and\nthe fifth they are forgotten. But if we look more closely, we see that\nwhat thus succumb are the theories properly so called, those which\npretend to teach us what things are. But there is in them something\nwhich usually survives. If one of them taught us a true relation, this\nrelation is definitively acquired, and it will be found again under a\nnew disguise in the other theories which will successively come to reign\nin place of the old.\n\nTake only a single example: The theory of the undulations of the ether\ntaught us that light is a motion; to-day fashion favors the\nelectromagnetic theory which teaches us that light is a current. We do\nnot consider whether we could reconcile them and say that light is a\ncurrent, and that this current is a motion. As it is probable in any\ncase that this motion would not be identical with that which the\npartisans of the old theory presume, we might think ourselves justified\nin saying that this old theory is dethroned. And yet something of it\nremains, since between the hypothetical currents which Maxwell supposes\nthere are the same relations as between the hypothetical motions that\nFresnel supposed. There is, therefore, something which remains over and\nthis something is the essential. This it is which explains how we see\nthe present physicists pass without any embarrassment from the language\nof Fresnel to that of Maxwell. Doubtless many connections that were\nbelieved well established have been abandoned, but the greatest number\nremain and it would seem must remain.\n\nAnd for these, then, what is the measure of their objectivity? Well, it\nis precisely the same as for our belief in external objects. These\nlatter are real in this, that the sensations they make us feel appear to\nus as united to each other by I know not what indestructible cement and\nnot by the hazard of a day. In the same way science reveals to us\nbetween phenomena other bonds finer but not less solid; these are\nthreads so slender that they long remained unperceived, but once noticed\nthere remains no way of not seeing them; they are therefore not less\nreal than those which give their reality to external objects; small\nmatter that they are more recently known, since neither can perish\nbefore the other.\n\nIt may be said, for instance, that the ether is no less real than any\nexternal body; to say this body exists is to say there is between the\ncolor of this body, its taste, its smell, an intimate bond, solid and\npersistent; to say the ether exists is to say there is a natural kinship\nbetween all the optical phenomena, and neither of the two propositions\nhas less value than the other.\n\nAnd the scientific syntheses have in a sense even more reality than\nthose of the ordinary senses, since they embrace more terms and tend to\nabsorb in them the partial syntheses.\n\nIt will be said that science is only a classification and that a\nclassification can not be true, but convenient. But it is true that it\nis convenient, it is true that it is so not only for me, but for all\nmen; it is true that it will remain convenient for our descendants; it\nis true finally that this can not be by chance.\n\nIn sum, the sole objective reality consists in the relations of things\nwhence results the universal harmony. Doubtless these relations, this\nharmony, could not be conceived outside of a mind which conceives them.\nBut they are nevertheless objective because they are, will become, or\nwill remain, common to all thinking beings.\n\nThis will permit us to revert to the question of the rotation of the\nearth which will give us at the same time a chance to make clear what\nprecedes by an example.\n\n\n7. _The Rotation of the Earth_\n\n\"... Therefore,\" have I said in _Science and Hypothesis_, \"this\naffirmation, the earth turns round, has no meaning ... or rather these\ntwo propositions, the earth turns round, and, it is more convenient to\nsuppose that the earth turns round, have one and the same meaning.\"\n\nThese words have given rise to the strangest interpretations. Some have\nthought they saw in them the rehabilitation of Ptolemy's system, and\nperhaps the justification of Galileo's condemnation.\n\nThose who had read attentively the whole volume could not, however,\ndelude themselves. This truth, the earth turns round, was put on the\nsame footing as Euclid's postulate, for example. Was that to reject it?\nBut better; in the same language it may very well be said: These two\npropositions, the external world exists, or, it is more convenient to\nsuppose that it exists, have one and the same meaning. So the hypothesis\nof the rotation of the earth would have the same degree of certitude as\nthe very existence of external objects.\n\nBut after what we have just explained in the fourth part, we may go\nfarther. A physical theory, we have said, is by so much the more true as\nit puts in evidence more true relations. In the light of this new\nprinciple, let us examine the question which occupies us.\n\nNo, there is no absolute space; these two contradictory propositions:\n'The earth turns round' and 'The earth does not turn round' are,\ntherefore, neither of them more true than the other. To affirm one while\ndenying the other, _in the kinematic sense_, would be to admit the\nexistence of absolute space.\n\nBut if the one reveals true relations that the other hides from us, we\ncan nevertheless regard it as physically more true than the other, since\nit has a richer content. Now in this regard no doubt is possible.\n\nBehold the apparent diurnal motion of the stars, and the diurnal motion\nof the other heavenly bodies, and besides, the flattening of the earth,\nthe rotation of Foucault's pendulum, the gyration of cyclones, the\ntrade-winds, what not else? For the Ptolemaist all these phenomena have\nno bond between them; for the Copernican they are produced by the one\nsame cause. In saying, the earth turns round, I affirm that all these\nphenomena have an intimate relation, and _that is true_, and that\nremains true, although there is not and can not be absolute space.\n\nSo much for the rotation of the earth upon itself; what shall we say of\nits revolution around the sun? Here again, we have three phenomena which\nfor the Ptolemaist are absolutely independent and which for the\nCopernican are referred back to the same origin; they are the apparent\ndisplacements of the planets on the celestial sphere, the aberration of\nthe fixed stars, the parallax of these same stars. Is it by chance that\nall the planets admit an inequality whose period is a year, and that\nthis period is precisely equal to that of aberration, precisely equal\nbesides to that of parallax? To adopt Ptolemy's system is to answer,\nyes; to adopt that of Copernicus is to answer, no; this is to affirm\nthat there is a bond between the three phenomena, and that also is true,\nalthough there is no absolute space.\n\nIn Ptolemy's system, the motions of the heavenly bodies can not be\nexplained by the action of central forces, celestial mechanics is\nimpossible. The intimate relations that celestial mechanics reveals to\nus between all the celestial phenomena are true relations; to affirm the\nimmobility of the earth would be to deny these relations, that would be\nto fool ourselves.\n\nThe truth for which Galileo suffered remains, therefore, the truth,\nalthough it has not altogether the same meaning as for the vulgar, and\nits true meaning is much more subtle, more profound and more rich.\n\n\n8. _Science for Its Own Sake_\n\nNot against M. LeRoy do I wish to defend science for its own sake; maybe\nthis is what he condemns, but this is what he cultivates, since he loves\nand seeks truth and could not live without it. But I have some thoughts\nto express.\n\nWe can not know all facts and it is necessary to choose those which are\nworthy of being known. According to Tolstoi, scientists make this choice\nat random, instead of making it, which would be reasonable, with a view\nto practical applications. On the contrary, scientists think that\ncertain facts are more interesting than others, because they complete an\nunfinished harmony, or because they make one foresee a great number of\nother facts. If they are wrong, if this hierarchy of facts that they\nimplicitly postulate is only an idle illusion, there could be no science\nfor its own sake, and consequently there could be no science. As for me,\nI believe they are right, and, for example, I have shown above what is\nthe high value of astronomical facts, not because they are capable of\npractical applications, but because they are the most instructive of\nall.\n\nIt is only through science and art that civilization is of value. Some\nhave wondered at the formula: science for its own sake; and yet it is as\ngood as life for its own sake, if life is only misery; and even as\nhappiness for its own sake, if we do not believe that all pleasures are\nof the same quality, if we do not wish to admit that the goal of\ncivilization is to furnish alcohol to people who love to drink.\n\nEvery act should have an aim. We must suffer, we must work, we must pay\nfor our place at the game, but this is for seeing's sake; or at the very\nleast that others may one day see.\n\nAll that is not thought is pure nothingness; since we can think only\nthoughts and all the words we use to speak of things can express only\nthoughts, to say there is something other than thought, is therefore an\naffirmation which can have no meaning.\n\nAnd yet--strange contradiction for those who believe in time--geologic\nhistory shows us that life is only a short episode between two\neternities of death, and that, even in this episode, conscious thought\nhas lasted and will last only a moment. Thought is only a gleam in the\nmidst of a long night.\n\nBut it is this gleam which is everything.\n\n\n * * * * *\n\n\n\n\nSCIENCE AND METHOD\n\n\n\n\n * * * * *\n\n\n\n\nINTRODUCTION\n\n\nI bring together here different studies relating more or less directly\nto questions of scientific methodology. The scientific method consists\nin observing and experimenting; if the scientist had at his disposal\ninfinite time, it would only be necessary to say to him: 'Look and\nnotice well'; but, as there is not time to see everything, and as it is\nbetter not to see than to see wrongly, it is necessary for him to make\nchoice. The first question, therefore, is how he should make this\nchoice. This question presents itself as well to the physicist as to the\nhistorian; it presents itself equally to the mathematician, and the\nprinciples which should guide each are not without analogy. The\nscientist conforms to them instinctively, and one can, reflecting on\nthese principles, foretell the future of mathematics.\n\nWe shall understand them better yet if we observe the scientist at work,\nand first of all it is necessary to know the psychologic mechanism of\ninvention and, in particular, that of mathematical creation. Observation\nof the processes of the work of the mathematician is particularly\ninstructive for the psychologist.\n\nIn all the sciences of observation account must be taken of the errors\ndue to the imperfections of our senses and our instruments. Luckily, we\nmay assume that, under certain conditions, these errors are in part\nself-compensating, so as to disappear in the average; this compensation\nis due to chance. But what is chance? This idea is difficult to justify\nor even to define; and yet what I have just said about the errors of\nobservation, shows that the scientist can not neglect it. It therefore\nis necessary to give a definition as precise as possible of this\nconcept, so indispensable yet so illusive.\n\nThese are generalities applicable in sum to all the sciences; and for\nexample the mechanism of mathematical invention does not differ sensibly\nfrom the mechanism of invention in general. Later I attack questions\nrelating more particularly to certain special sciences and first to pure\nmathematics.\n\nIn the chapters devoted to these, I have to treat subjects a little more\nabstract. I have first to speak of the notion of space; every one knows\nspace is relative, or rather every one says so, but many think still as\nif they believed it absolute; it suffices to reflect a little however to\nperceive to what contradictions they are exposed.\n\nThe questions of teaching have their importance, first in themselves,\nthen because reflecting on the best way to make new ideas penetrate\nvirgin minds is at the same time reflecting on how these notions were\nacquired by our ancestors, and consequently on their true origin, that\nis to say, in reality on their true nature. Why do children usually\nunderstand nothing of the definitions which satisfy scientists? Why is\nit necessary to give them others? This is the question I set myself in\nthe succeeding chapter and whose solution should, I think, suggest\nuseful reflections to the philosophers occupied with the logic of the\nsciences.\n\nOn the other hand, many geometers believe we can reduce mathematics to\nthe rules of formal logic. Unheard-of efforts have been made to do this;\nto accomplish it, some have not hesitated, for example, to reverse the\nhistoric order of the genesis of our conceptions and to try to explain\nthe finite by the infinite. I believe I have succeeded in showing, for\nall those who attack the problem unprejudiced, that here there is a\nfallacious illusion. I hope the reader will understand the importance of\nthe question and pardon me the aridity of the pages devoted to it.\n\nThe concluding chapters relative to mechanics and astronomy will be\neasier to read.\n\nMechanics seems on the point of undergoing a complete revolution. Ideas\nwhich appeared best established are assailed by bold innovators.\nCertainly it would be premature to decide in their favor at once simply\nbecause they are innovators.\n\nBut it is of interest to make known their doctrines, and this is what I\nhave tried to do. As far as possible I have followed the historic order;\nfor the new ideas would seem too astonishing unless we saw how they\narose.\n\nAstronomy offers us majestic spectacles and raises gigantic problems. We\ncan not dream of applying to them directly the experimental method; our\nlaboratories are too small. But analogy with phenomena these\nlaboratories permit us to attain may nevertheless guide the astronomer.\nThe Milky Way, for example, is an assemblage of suns whose movements\nseem at first capricious. But may not this assemblage be compared to\nthat of the molecules of a gas, whose properties the kinetic theory of\ngases has made known to us? It is thus by a roundabout way that the\nmethod of the physicist may come to the aid of the astronomer.\n\nFinally I have endeavored to give in a few lines the history of the\ndevelopment of French geodesy; I have shown through what persevering\nefforts, and often what dangers, the geodesists have procured for us the\nknowledge we have of the figure of the earth. Is this then a question of\nmethod? Yes, without doubt, this history teaches us in fact by what\nprecautions it is necessary to surround a serious scientific operation\nand how much time and pains it costs to conquer one new decimal.\n\n\n\n\nBOOK I\n\n\nSCIENCE AND THE SCIENTIST\n\n\n\n\nCHAPTER I\n\nTHE CHOICE OF FACTS\n\n\nTolstoi somewhere explains why 'science for its own sake' is in his eyes\nan absurd conception. We can not know _all_ facts, since their number is\npractically infinite. It is necessary to choose; then we may let this\nchoice depend on the pure caprice of our curiosity; would it not be\nbetter to let ourselves be guided by utility, by our practical and above\nall by our moral needs; have we nothing better to do than to count the\nnumber of lady-bugs on our planet?\n\nIt is clear the word utility has not for him the sense men of affairs\ngive it, and following them most of our contemporaries. Little cares he\nfor industrial applications, for the marvels of electricity or of\nautomobilism, which he regards rather as obstacles to moral progress;\nutility for him is solely what can make man better.\n\nFor my part, it need scarce be said, I could never be content with\neither the one or the other ideal; I want neither that plutocracy\ngrasping and mean, nor that democracy goody and mediocre, occupied\nsolely in turning the other cheek, where would dwell sages without\ncuriosity, who, shunning excess, would not die of disease, but would\nsurely die of ennui. But that is a matter of taste and is not what I\nwish to discuss.\n\nThe question nevertheless remains and should fix our attention; if our\nchoice can only be determined by caprice or by immediate utility, there\ncan be no science for its own sake, and consequently no science. But is\nthat true? That a choice must be made is incontestable; whatever be our\nactivity, facts go quicker than we, and we can not catch them; while the\nscientist discovers one fact, there happen milliards of milliards in a\ncubic millimeter of his body. To wish to comprise nature in science\nwould be to want to put the whole into the part.\n\nBut scientists believe there is a hierarchy of facts and that among them\nmay be made a judicious choice. They are right, since otherwise there\nwould be no science, yet science exists. One need only open the eyes to\nsee that the conquests of industry which have enriched so many practical\nmen would never have seen the light, if these practical men alone had\nexisted and if they had not been preceded by unselfish devotees who died\npoor, who never thought of utility, and yet had a guide far other than\ncaprice.\n\nAs Mach says, these devotees have spared their successors the trouble of\nthinking. Those who might have worked solely in view of an immediate\napplication would have left nothing behind them, and, in face of a new\nneed, all must have been begun over again. Now most men do not love to\nthink, and this is perhaps fortunate when instinct guides them, for most\noften, when they pursue an aim which is immediate and ever the same,\ninstinct guides them better than reason would guide a pure intelligence.\nBut instinct is routine, and if thought did not fecundate it, it would\nno more progress in man than in the bee or ant. It is needful then to\nthink for those who love not thinking, and, as they are numerous, it is\nneedful that each of our thoughts be as often useful as possible, and\nthis is why a law will be the more precious the more general it is.\n\nThis shows us how we should choose: the most interesting facts are those\nwhich may serve many times; these are the facts which have a chance of\ncoming up again. We have been so fortunate as to be born in a world\nwhere there are such. Suppose that instead of 60 chemical elements there\nwere 60 milliards of them, that they were not some common, the others\nrare, but that they were uniformly distributed. Then, every time we\npicked up a new pebble there would be great probability of its being\nformed of some unknown substance; all that we knew of other pebbles\nwould be worthless for it; before each new object we should be as the\nnew-born babe; like it we could only obey our caprices or our needs.\nBiologists would be just as much at a loss if there were only\nindividuals and no species and if heredity did not make sons like their\nfathers.\n\nIn such a world there would be no science; perhaps thought and even life\nwould be impossible, since evolution could not there develop the\npreservational instincts. Happily it is not so; like all good fortune to\nwhich we are accustomed, this is not appreciated at its true worth.\n\nWhich then are the facts likely to reappear? They are first the simple\nfacts. It is clear that in a complex fact a thousand circumstances are\nunited by chance, and that only a chance still much less probable could\nreunite them anew. But are there any simple facts? And if there are, how\nrecognize them? What assurance is there that a thing we think simple\ndoes not hide a dreadful complexity? All we can say is that we ought to\nprefer the facts which _seem_ simple to those where our crude eye\ndiscerns unlike elements. And then one of two things: either this\nsimplicity is real, or else the elements are so intimately mingled as\nnot to be distinguishable. In the first case there is chance of our\nmeeting anew this same simple fact, either in all its purity or entering\nitself as element in a complex manifold. In the second case this\nintimate mixture has likewise more chances of recurring than a\nheterogeneous assemblage; chance knows how to mix, it knows not how to\ndisentangle, and to make with multiple elements a well-ordered edifice\nin which something is distinguishable, it must be made expressly. The\nfacts which appear simple, even if they are not so, will therefore be\nmore easily revived by chance. This it is which justifies the method\ninstinctively adopted by the scientist, and what justifies it still\nbetter, perhaps, is that oft-recurring facts appear to us simple,\nprecisely because we are used to them.\n\nBut where is the simple fact? Scientists have been seeking it in the two\nextremes, in the infinitely great and in the infinitely small. The\nastronomer has found it because the distances of the stars are immense,\nso great that each of them appears but as a point, so great that the\nqualitative differences are effaced, and because a point is simpler than\na body which has form and qualities. The physicist on the other hand has\nsought the elementary phenomenon in fictively cutting up bodies into\ninfinitesimal cubes, because the conditions of the problem, which\nundergo slow and continuous variation in passing from one point of the\nbody to another, may be regarded as constant in the interior of each of\nthese little cubes. In the same way the biologist has been instinctively\nled to regard the cell as more interesting than the whole animal, and\nthe outcome has shown his wisdom, since cells belonging to organisms the\nmost different are more alike, for the one who can recognize their\nresemblances, than are these organisms themselves. The sociologist is\nmore embarrassed; the elements, which for him are men, are too unlike,\ntoo variable, too capricious, in a word, too complex; besides, history\nnever begins over again. How then choose the interesting fact, which is\nthat which begins again? Method is precisely the choice of facts; it is\nneedful then to be occupied first with creating a method, and many have\nbeen imagined, since none imposes itself, so that sociology is the\nscience which has the most methods and the fewest results.\n\nTherefore it is by the regular facts that it is proper to begin; but\nafter the rule is well established, after it is beyond all doubt, the\nfacts in full conformity with it are erelong without interest since they\nno longer teach us anything new. It is then the exception which becomes\nimportant. We cease to seek resemblances; we devote ourselves above all\nto the differences, and among the differences are chosen first the most\naccentuated, not only because they are the most striking, but because\nthey will be the most instructive. A simple example will make my thought\nplainer: Suppose one wishes to determine a curve by observing some of\nits points. The practician who concerns himself only with immediate\nutility would observe only the points he might need for some special\nobject. These points would be badly distributed on the curve; they would\nbe crowded in certain regions, rare in others, so that it would be\nimpossible to join them by a continuous line, and they would be\nunavailable for other applications. The scientist will proceed\ndifferently; as he wishes to study the curve for itself, he will\ndistribute regularly the points to be observed, and when enough are\nknown he will join them by a regular line and then he will have the\nentire curve. But for that how does he proceed? If he has determined an\nextreme point of the curve, he does not stay near this extremity, but\ngoes first to the other end; after the two extremities the most\ninstructive point will be the mid-point, and so on.\n\nSo when a rule is established we should first seek the cases where this\nrule has the greatest chance of failing. Thence, among other reasons,\ncome the interest of astronomic facts, and the interest of the geologic\npast; by going very far away in space or very far away in time, we may\nfind our usual rules entirely overturned, and these grand overturnings\naid us the better to see or the better to understand the little changes\nwhich may happen nearer to us, in the little corner of the world where\nwe are called to live and act. We shall better know this corner for\nhaving traveled in distant countries with which we have nothing to do.\n\nBut what we ought to aim at is less the ascertainment of resemblances\nand differences than the recognition of likenesses hidden under apparent\ndivergences. Particular rules seem at first discordant, but looking more\nclosely we see in general that they resemble each other; different as to\nmatter, they are alike as to form, as to the order of their parts. When\nwe look at them with this bias, we shall see them enlarge and tend to\nembrace everything. And this it is which makes the value of certain\nfacts which come to complete an assemblage and to show that it is the\nfaithful image of other known assemblages.\n\nI will not further insist, but these few words suffice to show that the\nscientist does not choose at random the facts he observes. He does not,\nas Tolstoi says, count the lady-bugs, because, however interesting\nlady-bugs may be, their number is subject to capricious variations. He\nseeks to condense much experience and much thought into a slender\nvolume; and that is why a little book on physics contains so many past\nexperiences and a thousand times as many possible experiences whose\nresult is known beforehand.\n\nBut we have as yet looked at only one side of the question. The\nscientist does not study nature because it is useful; he studies it\nbecause he delights in it, and he delights in it because it is\nbeautiful. If nature were not beautiful, it would not be worth knowing,\nand if nature were not worth knowing, life would not be worth living. Of\ncourse I do not here speak of that beauty which strikes the senses, the\nbeauty of qualities and of appearances; not that I undervalue such\nbeauty, far from it, but it has nothing to do with science; I mean that\nprofounder beauty which comes from the harmonious order of the parts\nand which a pure intelligence can grasp. This it is which gives body, a\nstructure so to speak, to the iridescent appearances which flatter our\nsenses, and without this support the beauty of these fugitive dreams\nwould be only imperfect, because it would be vague and always fleeting.\nOn the contrary, intellectual beauty is sufficient unto itself, and it\nis for its sake, more perhaps than for the future good of humanity, that\nthe scientist devotes himself to long and difficult labors.\n\nIt is, therefore, the quest of this especial beauty, the sense of the\nharmony of the cosmos, which makes us choose the facts most fitting to\ncontribute to this harmony, just as the artist chooses from among the\nfeatures of his model those which perfect the picture and give it\ncharacter and life. And we need not fear that this instinctive and\nunavowed prepossession will turn the scientist aside from the search for\nthe true. One may dream a harmonious world, but how far the real world\nwill leave it behind! The greatest artists that ever lived, the Greeks,\nmade their heavens; how shabby it is beside the true heavens, ours!\n\nAnd it is because simplicity, because grandeur, is beautiful, that we\npreferably seek simple facts, sublime facts, that we delight now to\nfollow the majestic course of the stars, now to examine with the\nmicroscope that prodigious littleness which is also a grandeur, now to\nseek in geologic time the traces of a past which attracts because it is\nfar away.\n\nWe see too that the longing for the beautiful leads us to the same\nchoice as the longing for the useful. And so it is that this economy of\nthought, this economy of effort, which is, according to Mach, the\nconstant tendency of science, is at the same time a source of beauty and\na practical advantage. The edifices that we admire are those where the\narchitect has known how to proportion the means to the end, where the\ncolumns seem to carry gaily, without effort, the weight placed upon\nthem, like the gracious caryatids of the Erechtheum.\n\nWhence comes this concordance? Is it simply that the things which seem\nto us beautiful are those which best adapt themselves to our\nintelligence, and that consequently they are at the same time the\nimplement this intelligence knows best how to use? Or is there here a\nplay of evolution and natural selection? Have the peoples whose ideal\nmost conformed to their highest interest exterminated the others and\ntaken their place? All pursued their ideals without reference to\nconsequences, but while this quest led some to destruction, to others it\ngave empire. One is tempted to believe it. If the Greeks triumphed over\nthe barbarians and if Europe, heir of Greek thought, dominates the\nworld, it is because the savages loved loud colors and the clamorous\ntones of the drum which occupied only their senses, while the Greeks\nloved the intellectual beauty which hides beneath sensuous beauty, and\nthis intellectual beauty it is which makes intelligence sure and strong.\n\nDoubtless such a triumph would horrify Tolstoi, and he would not like to\nacknowledge that it might be truly useful. But this disinterested quest\nof the true for its own beauty is sane also and able to make man better.\nI well know that there are mistakes, that the thinker does not always\ndraw thence the serenity he should find therein, and even that there are\nscientists of bad character. Must we, therefore, abandon science and\nstudy only morals? What! Do you think the moralists themselves are\nirreproachable when they come down from their pedestal?\n\n\n\n\nCHAPTER II\n\nTHE FUTURE OF MATHEMATICS\n\n\nTo foresee the future of mathematics, the true method is to study its\nhistory and its present state.\n\nIs this not for us mathematicians in a way a professional procedure? We\nare accustomed to _extrapolate_, which is a means of deducing the future\nfrom the past and present, and as we well know what this amounts to, we\nrun no risk of deceiving ourselves about the range of the results it\ngives us.\n\nWe have had hitherto prophets of evil. They blithely reiterate that all\nproblems capable of solution have already been solved, and that nothing\nis left but gleaning. Happily the case of the past reassures us. Often\nit was thought all problems were solved or at least an inventory was\nmade of all admitting solution. And then the sense of the word solution\nenlarged, the insoluble problems became the most interesting of all, and\nothers unforeseen presented themselves. For the Greeks a good solution\nwas one employing only ruler and compasses; then it became one obtained\nby the extraction of roots, then one using only algebraic or logarithmic\nfunctions. The pessimists thus found themselves always outflanked,\nalways forced to retreat, so that at present I think there are no more.\n\nMy intention, therefore, is not to combat them, as they are dead; we\nwell know that mathematics will continue to develop, but the question is\nhow, in what direction? You will answer, 'in every direction,' and that\nis partly true; but if it were wholly true it would be a little\nappalling. Our riches would soon become encumbering and their\naccumulation would produce a medley as impenetrable as the unknown true\nwas for the ignorant.\n\nThe historian, the physicist, even, must make a choice among facts; the\nhead of the scientist, which is only a corner of the universe, could\nnever contain the universe entire; so that among the innumerable facts\nnature offers, some will be passed by, others retained.\n\nJust so, _a fortiori_, in mathematics; no more can the geometer hold\nfast pell-mell all the facts presenting themselves to him; all the more\nbecause he it is, almost I had said his caprice, that creates these\nfacts. He constructs a wholly new combination by putting together its\nelements; nature does not in general give it to him ready made.\n\nDoubtless it sometimes happens that the mathematician undertakes a\nproblem to satisfy a need in physics; that the physicist or engineer\nasks him to calculate a number for a certain application. Shall it be\nsaid that we geometers should limit ourselves to awaiting orders, and,\nin place of cultivating our science for our own delectation, try only to\naccommodate ourselves to the wants of our patrons? If mathematics has no\nother object besides aiding those who study nature, it is from these we\nshould await orders. Is this way of looking at it legitimate? Certainly\nnot; if we had not cultivated the exact sciences for themselves, we\nshould not have created mathematics the instrument, and the day the call\ncame from the physicist we should have been helpless.\n\nNor do the physicists wait to study a phenomenon until some urgent need\nof material life has made it a necessity for them; and they are right.\nIf the scientists of the eighteenth century had neglected electricity as\nbeing in their eyes only a curiosity without practical interest, we\nshould have had in the twentieth century neither telegraphy, nor\nelectro-chemistry, nor electro-technics. The physicists, compelled to\nchoose, are therefore not guided in their choice solely by utility. How\nthen do they choose between the facts of nature? We have explained it in\nthe preceding chapter: the facts which interest them are those capable\nof leading to the discovery of a law, and so they are analogous to many\nother facts which do not seem to us isolated, but closely grouped with\nothers. The isolated fact attracts all eyes, those of the layman as well\nas of the scientist. But what the genuine physicist alone knows how to\nsee, is the bond which unites many facts whose analogy is profound but\nhidden. The story of Newton's apple is probably not true, but it is\nsymbolic; let us speak of it then as if it were true. Well then, we must\nbelieve that before Newton plenty of men had seen apples fall; not one\nknew how to conclude anything therefrom. Facts would be sterile were\nthere not minds capable of choosing among them, discerning those behind\nwhich something was hidden, and of recognizing what is hiding, minds\nwhich under the crude fact perceive the soul of the fact.\n\nWe find just the same thing in mathematics. From the varied elements at\nour disposal we can get millions of different combinations; but one of\nthese combinations, in so far as it is isolated, is absolutely void of\nvalue. Often we have taken great pains to construct it, but it serves no\npurpose, if not perhaps to furnish a task in secondary education. Quite\notherwise will it be when this combination shall find place in a class\nof analogous combinations and we shall have noticed this analogy. We are\nno longer in the presence of a fact, but of a law. And upon that day the\nreal discoverer will not be the workman who shall have patiently built\nup certain of these combinations; it will be he who brings to light\ntheir kinship. The first will have seen merely the crude fact, only the\nother will have perceived the soul of the fact. Often to fix this\nkinship it suffices him to make a new word, and this word is creative.\nThe history of science furnishes us a crowd of examples familiar to all.\n\nThe celebrated Vienna philosopher Mach has said that the r\u00f4le of science\nis to produce economy of thought, just as machines produce economy of\neffort. And that is very true. The savage reckons on his fingers or by\nheaping pebbles. In teaching children the multiplication table we spare\nthem later innumerable pebble bunchings. Some one has already found out,\nwith pebbles or otherwise, that 6 times 7 is 42 and has had the idea of\nnoting the result, and so we need not do it over again. He did not waste\nhis time even if he reckoned for pleasure: his operation took him only\ntwo minutes; it would have taken in all two milliards if a milliard men\nhad had to do it over after him.\n\nThe importance of a fact then is measured by its yield, that is to say,\nby the amount of thought it permits us to spare.\n\nIn physics the facts of great yield are those entering into a very\ngeneral law, since from it they enable us to foresee a great number of\nothers, and just so it is in mathematics. Suppose I have undertaken a\ncomplicated calculation and laboriously reached a result: I shall not\nbe compensated for my trouble if thereby I have not become capable of\nforeseeing the results of other analogous calculations and guiding them\nwith a certainty that avoids the gropings to which one must be resigned\nin a first attempt. On the other hand, I shall not have wasted my time\nif these gropings themselves have ended by revealing to me the profound\nanalogy of the problem just treated with a much more extended class of\nother problems; if they have shown me at once the resemblances and\ndifferences of these, if in a word they have made me perceive the\npossibility of a generalization. Then it is not a new result I have won,\nit is a new power.\n\nThe simple example that comes first to mind is that of an algebraic\nformula which gives us the solution of a type of numeric problems when\nfinally we replace the letters by numbers. Thanks to it, a single\nalgebraic calculation saves us the pains of ceaselessly beginning over\nagain new numeric calculations. But this is only a crude example; we all\nknow there are analogies inexpressible by a formula and all the more\nprecious.\n\nA new result is of value, if at all, when in unifying elements long\nknown but hitherto separate and seeming strangers one to another it\nsuddenly introduces order where apparently disorder reigned. It then\npermits us to see at a glance each of these elements and its place in\nthe assemblage. This new fact is not merely precious by itself, but it\nalone gives value to all the old facts it combines. Our mind is weak as\nare the senses; it would lose itself in the world's complexity were this\ncomplexity not harmonious; like a near-sighted person, it would see only\nthe details and would be forced to forget each of these details before\nexamining the following, since it would be incapable of embracing all.\nThe only facts worthy our attention are those which introduce order into\nthis complexity and so make it accessible.\n\nMathematicians attach great importance to the elegance of their methods\nand their results. This is not pure dilettantism. What is it indeed that\ngives us the feeling of elegance in a solution, in a demonstration? It\nis the harmony of the diverse parts, their symmetry, their happy\nbalance; in a word it is all that introduces order, all that gives\nunity, that permits us to see clearly and to comprehend at once both the\n_ensemble_ and the details. But this is exactly what yields great\nresults; in fact the more we see this aggregate clearly and at a single\nglance, the better we perceive its analogies with other neighboring\nobjects, consequently the more chances we have of divining the possible\ngeneralizations. Elegance may produce the feeling of the unforeseen by\nthe unexpected meeting of objects we are not accustomed to bring\ntogether; there again it is fruitful, since it thus unveils for us\nkinships before unrecognized. It is fruitful even when it results only\nfrom the contrast between the simplicity of the means and the complexity\nof the problem set; it makes us then think of the reason for this\ncontrast and very often makes us see that chance is not the reason; that\nit is to be found in some unexpected law. In a word, the feeling of\nmathematical elegance is only the satisfaction due to any adaptation of\nthe solution to the needs of our mind, and it is because of this very\nadaptation that this solution can be for us an instrument. Consequently\nthis esthetic satisfaction is bound up with the economy of thought.\nAgain the comparison of the Erechtheum comes to my mind, but I must not\nuse it too often.\n\nIt is for the same reason that, when a rather long calculation has led\nto some simple and striking result, we are not satisfied until we have\nshown that we should have been _able to foresee_, if not this entire\nresult, at least its most characteristic traits. Why? What prevents our\nbeing content with a calculation which has told us, it seems, all we\nwished to know? It is because, in analogous cases, the long calculation\nmight not again avail, and that this is not so about the reasoning often\nhalf intuitive which would have enabled us to foresee. This reasoning\nbeing short, we see at a single glance all its parts, so that we\nimmediately perceive what must be changed to adapt it to all the\nproblems of the same nature which can occur. And then it enables us to\nforesee if the solution of these problems will be simple, it shows us at\nleast if the calculation is worth undertaking.\n\nWhat we have just said suffices to show how vain it would be to seek to\nreplace by any mechanical procedure the free initiative of the\nmathematician. To obtain a result of real value, it is not enough to\ngrind out calculations, or to have a machine to put things in order; it\nis not order alone, it is unexpected order, which is worth while. The\nmachine may gnaw on the crude fact, the soul of the fact will always\nescape it.\n\nSince the middle of the last century, mathematicians are more and more\ndesirous of attaining absolute rigor; they are right, and this tendency\nwill be more and more accentuated. In mathematics rigor is not\neverything, but without it there is nothing. A demonstration which is\nnot rigorous is nothingness. I think no one will contest this truth. But\nif it were taken too literally, we should be led to conclude that before\n1820, for example, there was no mathematics; this would be manifestly\nexcessive; the geometers of that time understood voluntarily what we\nexplain by prolix discourse. This does not mean that they did not see it\nat all; but they passed over it too rapidly, and to see it well would\nhave necessitated taking the pains to say it.\n\nBut is it always needful to say it so many times? Those who were the\nfirst to emphasize exactness before all else have given us arguments\nthat we may try to imitate; but if the demonstrations of the future are\nto be built on this model, mathematical treatises will be very long; and\nif I fear the lengthenings, it is not solely because I deprecate\nencumbering libraries, but because I fear that in being lengthened out,\nour demonstrations may lose that appearance of harmony whose usefulness\nI have just explained.\n\nThe economy of thought is what we should aim at, so it is not enough to\nsupply models for imitation. It is needful for those after us to be able\nto dispense with these models and, in place of repeating an argument\nalready made, summarize it in a few words. And this has already been\nattained at times. For instance, there was a type of reasoning found\neverywhere, and everywhere alike. They were perfectly exact but long.\nThen all at once the phrase 'uniformity of convergence' was hit upon and\nthis phrase made those arguments needless; we were no longer called upon\nto repeat them, since they could be understood. Those who conquer\ndifficulties then do us a double service: first they teach us to do as\nthey at need, but above all they enable us as often as possible to avoid\ndoing as they, yet without sacrifice of exactness.\n\nWe have just seen by one example the importance of words in mathematics,\nbut many others could be cited. It is hard to believe how much a\nwell-chosen word can economize thought, as Mach says. Perhaps I have\nalready said somewhere that mathematics is the art of giving the same\nname to different things. It is proper that these things, differing in\nmatter, be alike in form, that they may, so to speak, run in the same\nmold. When the language has been well chosen, we are astonished to see\nthat all the proofs made for a certain object apply immediately to many\nnew objects; there is nothing to change, not even the words, since the\nnames have become the same.\n\nA well-chosen word usually suffices to do away with the exceptions from\nwhich the rules stated in the old way suffer; this is why we have\ncreated negative quantities, imaginaries, points at infinity, and what\nnot. And exceptions, we must not forget, are pernicious because they\nhide the laws.\n\nWell, this is one of the characteristics by which we recognize the facts\nwhich yield great results. They are those which allow of these happy\ninnovations of language. The crude fact then is often of no great\ninterest; we may point it out many times without having rendered great\nservice to science. It takes value only when a wiser thinker perceives\nthe relation for which it stands, and symbolizes it by a word.\n\nMoreover the physicists do just the same. They have invented the word\n'energy,' and this word has been prodigiously fruitful, because it also\nmade the law by eliminating the exceptions, since it gave the same name\nto things differing in matter and like in form.\n\nAmong words that have had the most fortunate influence I would select\n'group' and 'invariant.' They have made us see the essence of many\nmathematical reasonings; they have shown us in how many cases the old\nmathematicians considered groups without knowing it, and how, believing\nthemselves far from one another, they suddenly found themselves near\nwithout knowing why.\n\nTo-day we should say that they had dealt with isomorphic groups. We now\nknow that in a group the matter is of little interest, the form alone\ncounts, and that when we know a group we thus know all the isomorphic\ngroups; and thanks to these words 'group' and 'isomorphism,' which\ncondense in a few syllables this subtile rule and quickly make it\nfamiliar to all minds, the transition is immediate and can be done with\nevery economy of thought effort. The idea of group besides attaches to\nthat of transformation. Why do we put such a value on the invention of a\nnew transformation? Because from a single theorem it enables us to get\nten or twenty; it has the same value as a zero adjoined to the right of\na whole number.\n\nThis then it is which has hitherto determined the direction of\nmathematical advance, and just as certainly will determine it in the\nfuture. But to this end the nature of the problems which come up\ncontributes equally. We can not forget what must be our aim. In my\nopinion this aim is double. Our science borders upon both philosophy and\nphysics, and we work for our two neighbors; so we have always seen and\nshall still see mathematicians advancing in two opposite directions.\n\nOn the one hand, mathematical science must reflect upon itself, and that\nis useful since reflecting on itself is reflecting on the human mind\nwhich has created it, all the more because it is the very one of its\ncreations for which it has borrowed least from without. This is why\ncertain mathematical speculations are useful, such as those devoted to\nthe study of the postulates, of unusual geometries, of peculiar\nfunctions. The more these speculations diverge from ordinary\nconceptions, and consequently from nature and applications, the better\nthey show us what the human mind can create when it frees itself more\nand more from the tyranny of the external world, the better therefore\nthey let us know it in itself.\n\nBut it is toward the other side, the side of nature, that we must direct\nthe bulk of our army. There we meet the physicist or the engineer, who\nsays to us: \"Please integrate this differential equation for me; I might\nneed it in a week in view of a construction which should be finished by\nthat time.\" \"This equation,\" we answer, \"does not come under one of the\nintegrable types; you know there are not many.\" \"Yes, I know; but then\nwhat good are you?\" Usually to understand each other is enough; the\nengineer in reality does not need the integral in finite terms; he\nneeds to know the general look of the integral function, or he simply\nwants a certain number which could readily be deduced from this integral\nif it were known. Usually it is not known, but the number can be\ncalculated without it if we know exactly what number the engineer needs\nand with what approximation.\n\nFormerly an equation was considered solved only when its solution had\nbeen expressed by aid of a finite number of known functions; but that is\npossible scarcely once in a hundred times. What we always can do, or\nrather what we should always seek to do, is to solve the problem\n_qualitatively_ so to speak; that is to say, seek to know the general\nform of the curve which represents the unknown function.\n\nIt remains to find the _quantitative_ solution of the problem; but if\nthe unknown can not be determined by a finite calculation, it may always\nbe represented by a convergent infinite series which enables us to\ncalculate it. Can that be regarded as a true solution? We are told that\nNewton sent Leibnitz an anagram almost like this: aaaaabbbeeeeij, etc.\nLeibnitz naturally understood nothing at all of it; but we, who have the\nkey, know that this anagram meant, translated into modern terms: \"I can\nintegrate all differential equations\"; and we are tempted to say that\nNewton had either great luck or strange delusions. He merely wished to\nsay he could form (by the method of indeterminate coefficients) a series\nof powers formally satisfying the proposed equation.\n\nSuch a solution would not satisfy us to-day, and for two reasons:\nbecause the convergence is too slow and because the terms follow each\nother without obeying any law. On the contrary, the series [Theta] seems\nto us to leave nothing to be desired, first because it converges very\nquickly (this is for the practical man who wishes to get at a number as\nquickly as possible) and next because we see at a glance the law of the\nterms (this is to satisfy the esthetic need of the theorist).\n\nBut then there are no longer solved problems and others which are not;\nthere are only problems _more or less_ solved, according as they are\nsolved by a series converging more or less rapidly, or ruled by a law\nmore or less harmonious. It often happens however that an imperfect\nsolution guides us toward a better one. Sometimes the series converges\nso slowly that the computation is impracticable and we have only\nsucceeded in proving the possibility of the problem.\n\nAnd then the engineer finds this a mockery, and justly, since it will\nnot aid him to complete his construction by the date fixed. He little\ncares to know if it will benefit engineers of the twenty-second century.\nBut as for us, we think differently and we are sometimes happier to have\nspared our grandchildren a day's work than to have saved our\ncontemporaries an hour.\n\nSometimes by groping, empirically, so to speak, we reach a formula\nsufficiently convergent. \"What more do you want?\" says the engineer. And\nyet, in spite of all, we are not satisfied; we should have liked _to\nforesee_ that convergence. Why? Because if we had known how to foresee\nit once, we would know how to foresee it another time. We have\nsucceeded; that is a small matter in our eyes if we can not validly\nexpect to do so again.\n\nIn proportion as science develops, its total comprehension becomes more\ndifficult; then we seek to cut it in pieces and to be satisfied with one\nof these pieces: in a word, to specialize. If we went on in this way, it\nwould be a grievous obstacle to the progress of science. As we have\nsaid, it is by unexpected union between its diverse parts that it\nprogresses. To specialize too much would be to forbid these drawings\ntogether. It is to be hoped that congresses like those of Heidelberg and\nRome, by putting us in touch with one another, will open for us vistas\nover neighboring domains and oblige us to compare them with our own, to\nrange somewhat abroad from our own little village; thus they will be the\nbest remedy for the danger just mentioned.\n\nBut I have lingered too long over generalities; it is time to enter into\ndetail.\n\nLet us pass in review the various special sciences which combined make\nmathematics; let us see what each has accomplished, whither it tends and\nwhat we may hope from it. If the preceding views are correct, we should\nsee that the greatest advances in the past have happened when two of\nthese sciences have united, when we have become conscious of the\nsimilarity of their form, despite the difference of their matter, when\nthey have so modeled themselves upon each other that each could profit\nby the other's conquests. We should at the same time foresee in\ncombinations of the same sort the progress of the future.\n\n\nARITHMETIC\n\nProgress in arithmetic has been much slower than in algebra and\nanalysis, and it is easy to see why. The feeling of continuity is a\nprecious guide which the arithmetician lacks; each whole number is\nseparated from the others--it has, so to speak, its own individuality.\nEach of them is a sort of exception and this is why general theorems are\nrarer in the theory of numbers; this is also why those which exist are\nmore hidden and longer elude the searchers.\n\nIf arithmetic is behind algebra and analysis, the best thing for it to\ndo is to seek to model itself upon these sciences so as to profit by\ntheir advance. The arithmetician ought therefore to take as guide the\nanalogies with algebra. These analogies are numerous and if, in many\ncases, they have not yet been studied sufficiently closely to become\nutilizable, they at least have long been foreseen, and even the language\nof the two sciences shows they have been recognized. Thus we speak of\ntranscendent numbers and thus we account for the future classification\nof these numbers already having as model the classification of\ntranscendent functions, and still we do not as yet very well see how to\npass from one classification to the other; but had it been seen, it\nwould already have been accomplished and would no longer be the work of\nthe future.\n\nThe first example that comes to my mind is the theory of congruences,\nwhere is found a perfect parallelism to the theory of algebraic\nequations. Surely we shall succeed in completing this parallelism, which\nmust hold for instance between the theory of algebraic curves and that\nof congruences with two variables. And when the problems relative to\ncongruences with several variables shall be solved, this will be a first\nstep toward the solution of many questions of indeterminate analysis.\n\n\nALGEBRA\n\nThe theory of algebraic equations will still long hold the attention of\ngeometers; numerous and very different are the sides whence it may be\nattacked.\n\nWe need not think algebra is ended because it gives us rules to form all\npossible combinations; it remains to find the interesting combinations,\nthose which satisfy such and such a condition. Thus will be formed a\nsort of indeterminate analysis where the unknowns will no longer be\nwhole numbers, but polynomials. This time it is algebra which will model\nitself upon arithmetic, following the analogy of the whole number to the\nintegral polynomial with any coefficients or to the integral polynomial\nwith integral coefficients.\n\n\nGEOMETRY\n\nIt looks as if geometry could contain nothing which is not already\nincluded in algebra or analysis; that geometric facts are only algebraic\nor analytic facts expressed in another language. It might then be\nthought that after our review there would remain nothing more for us to\nsay relating specially to geometry. This would be to fail to recognize\nthe importance of well-constructed language, not to comprehend what is\nadded to the things themselves by the method of expressing these things\nand consequently of grouping them.\n\nFirst the geometric considerations lead us to set ourselves new\nproblems; these may be, if you choose, analytic problems, but such as we\nnever would have set ourselves in connection with analysis. Analysis\nprofits by them however, as it profits by those it has to solve to\nsatisfy the needs of physics.\n\nA great advantage of geometry lies in the fact that in it the senses can\ncome to the aid of thought, and help find the path to follow, and many\nminds prefer to put the problems of analysis into geometric form.\nUnhappily our senses can not carry us very far, and they desert us when\nwe wish to soar beyond the classical three dimensions. Does this mean\nthat, beyond the restricted domain wherein they seem to wish to imprison\nus, we should rely only on pure analysis and that all geometry of more\nthan three dimensions is vain and objectless? The greatest masters of a\npreceding generation would have answered 'yes'; to-day we are so\nfamiliarized with this notion that we can speak of it, even in a\nuniversity course, without arousing too much astonishment.\n\nBut what good is it? That is easy to see: First it gives us a very\nconvenient terminology, which expresses concisely what the ordinary\nanalytic language would say in prolix phrases. Moreover, this language\nmakes us call like things by the same name and emphasize analogies it\nwill never again let us forget. It enables us therefore still to find\nour way in this space which is too big for us and which we can not see,\nalways recalling visible space, which is only an imperfect image of it\ndoubtless, but which is nevertheless an image. Here again, as in all the\npreceding examples, it is analogy with the simple which enables us to\ncomprehend the complex.\n\nThis geometry of more than three dimensions is not a simple analytic\ngeometry; it is not purely quantitative, but qualitative also, and it is\nin this respect above all that it becomes interesting. There is a\nscience called _analysis situs_ and which has for its object the study\nof the positional relations of the different elements of a figure, apart\nfrom their sizes. This geometry is purely qualitative; its theorems\nwould remain true if the figures, instead of being exact, were roughly\nimitated by a child. We may also make an _analysis situs_ of more than\nthree dimensions. The importance of _analysis situs_ is enormous and can\nnot be too much emphasized; the advantage obtained from it by Riemann,\none of its chief creators, would suffice to prove this. We must achieve\nits complete construction in the higher spaces; then we shall have an\ninstrument which will enable us really to see in hyperspace and\nsupplement our senses.\n\nThe problems of _analysis situs_ would perhaps not have suggested\nthemselves if the analytic language alone had been spoken; or rather, I\nam mistaken, they would have occurred surely, since their solution is\nessential to a crowd of questions in analysis, but they would have come\nsingly, one after another, and without our being able to perceive their\ncommon bond.\n\n\nCANTORISM\n\nI have spoken above of our need to go back continually to the first\nprinciples of our science, and of the advantage of this for the study of\nthe human mind. This need has inspired two endeavors which have taken a\nvery prominent place in the most recent annals of mathematics. The first\nis Cantorism, which has rendered our science such conspicuous service.\nCantor introduced into science a new way of considering mathematical\ninfinity. One of the characteristic traits of Cantorism is that in place\nof going up to the general by building up constructions more and more\ncomplicated and defining by construction, it starts from the _genus\nsupremum_ and defines only, as the scholastics would have said, _per\ngenus proximum et differentiam specificam_. Thence comes the horror it\nhas sometimes inspired in certain minds, for instance in Hermite, whose\nfavorite idea was to compare the mathematical to the natural sciences.\nWith most of us these prejudices have been dissipated, but it has come\nto pass that we have encountered certain paradoxes, certain apparent\ncontradictions that would have delighted Zeno, the Eleatic and the\nschool of Megara. And then each must seek the remedy. For my part, I\nthink, and I am not the only one, that the important thing is never to\nintroduce entities not completely definable in a finite number of words.\nWhatever be the cure adopted, we may promise ourselves the joy of the\ndoctor called in to follow a beautiful pathologic case.\n\n\nTHE INVESTIGATION OF THE POSTULATES\n\nOn the other hand, efforts have been made to enumerate the axioms and\npostulates, more or less hidden, which serve as foundation to the\ndifferent theories of mathematics. Professor Hilbert has obtained the\nmost brilliant results. It seems at first that this domain would be very\nrestricted and there would be nothing more to do when the inventory\nshould be ended, which could not take long. But when we shall have\nenumerated all, there will be many ways of classifying all; a good\nlibrarian always finds something to do, and each new classification will\nbe instructive for the philosopher.\n\nHere I end this review which I could not dream of making complete. I\nthink these examples will suffice to show by what mechanism the\nmathematical sciences have made their progress in the past and in what\ndirection they must advance in the future.\n\n\n\n\nCHAPTER III\n\nMATHEMATICAL CREATION\n\n\nThe genesis of mathematical creation is a problem which should intensely\ninterest the psychologist. It is the activity in which the human mind\nseems to take least from the outside world, in which it acts or seems to\nact only of itself and on itself, so that in studying the procedure of\ngeometric thought we may hope to reach what is most essential in man's\nmind.\n\nThis has long been appreciated, and some time back the journal called\n_L'enseignement math\u00e9matique_, edited by Laisant and Fehr, began an\ninvestigation of the mental habits and methods of work of different\nmathematicians. I had finished the main outlines of this article when\nthe results of that inquiry were published, so I have hardly been able\nto utilize them and shall confine myself to saying that the majority of\nwitnesses confirm my conclusions; I do not say all, for when the appeal\nis to universal suffrage unanimity is not to be hoped.\n\nA first fact should surprise us, or rather would surprise us if we were\nnot so used to it. How does it happen there are people who do not\nunderstand mathematics? If mathematics invokes only the rules of logic,\nsuch as are accepted by all normal minds; if its evidence is based on\nprinciples common to all men, and that none could deny without being\nmad, how does it come about that so many persons are here refractory?\n\nThat not every one can invent is nowise mysterious. That not every one\ncan retain a demonstration once learned may also pass. But that not\nevery one can understand mathematical reasoning when explained appears\nvery surprising when we think of it. And yet those who can follow this\nreasoning only with difficulty are in the majority: that is undeniable,\nand will surely not be gainsaid by the experience of secondary-school\nteachers.\n\nAnd further: how is error possible in mathematics? A sane mind should\nnot be guilty of a logical fallacy, and yet there are very fine minds\nwho do not trip in brief reasoning such as occurs in the ordinary doings\nof life, and who are incapable of following or repeating without error\nthe mathematical demonstrations which are longer, but which after all\nare only an accumulation of brief reasonings wholly analogous to those\nthey make so easily. Need we add that mathematicians themselves are not\ninfallible?\n\nThe answer seems to me evident. Imagine a long series of syllogisms, and\nthat the conclusions of the first serve as premises of the following: we\nshall be able to catch each of these syllogisms, and it is not in\npassing from premises to conclusion that we are in danger of deceiving\nourselves. But between the moment in which we first meet a proposition\nas conclusion of one syllogism, and that in which we reencounter it as\npremise of another syllogism occasionally some time will elapse, several\nlinks of the chain will have unrolled; so it may happen that we have\nforgotten it, or worse, that we have forgotten its meaning. So it may\nhappen that we replace it by a slightly different proposition, or that,\nwhile retaining the same enunciation, we attribute to it a slightly\ndifferent meaning, and thus it is that we are exposed to error.\n\nOften the mathematician uses a rule. Naturally he begins by\ndemonstrating this rule; and at the time when this proof is fresh in his\nmemory he understands perfectly its meaning and its bearing, and he is\nin no danger of changing it. But subsequently he trusts his memory and\nafterward only applies it in a mechanical way; and then if his memory\nfails him, he may apply it all wrong. Thus it is, to take a simple\nexample, that we sometimes make slips in calculation because we have\nforgotten our multiplication table.\n\nAccording to this, the special aptitude for mathematics would be due\nonly to a very sure memory or to a prodigious force of attention. It\nwould be a power like that of the whist-player who remembers the cards\nplayed; or, to go up a step, like that of the chess-player who can\nvisualize a great number of combinations and hold them in his memory.\nEvery good mathematician ought to be a good chess-player, and inversely;\nlikewise he should be a good computer. Of course that sometimes happens;\nthus Gauss was at the same time a geometer of genius and a very\nprecocious and accurate computer.\n\nBut there are exceptions; or rather I err; I can not call them\nexceptions without the exceptions being more than the rule. Gauss it is,\non the contrary, who was an exception. As for myself, I must confess, I\nam absolutely incapable even of adding without mistakes. In the same way\nI should be but a poor chess-player; I would perceive that by a certain\nplay I should expose myself to a certain danger; I would pass in review\nseveral other plays, rejecting them for other reasons, and then finally\nI should make the move first examined, having meantime forgotten the\ndanger I had foreseen.\n\nIn a word, my memory is not bad, but it would be insufficient to make me\na good chess-player. Why then does it not fail me in a difficult piece\nof mathematical reasoning where most chess-players would lose\nthemselves? Evidently because it is guided by the general march of the\nreasoning. A mathematical demonstration is not a simple juxtaposition of\nsyllogisms, it is syllogisms _placed in a certain order_, and the order\nin which these elements are placed is much more important than the\nelements themselves. If I have the feeling, the intuition, so to speak,\nof this order, so as to perceive at a glance the reasoning as a whole, I\nneed no longer fear lest I forget one of the elements, for each of them\nwill take its allotted place in the array, and that without any effort\nof memory on my part.\n\nIt seems to me then, in repeating a reasoning learned, that I could have\ninvented it. This is often only an illusion; but even then, even if I am\nnot so gifted as to create it by myself, I myself re-invent it in so far\nas I repeat it.\n\nWe know that this feeling, this intuition of mathematical order, that\nmakes us divine hidden harmonies and relations, can not be possessed by\nevery one. Some will not have either this delicate feeling so difficult\nto define, or a strength of memory and attention beyond the ordinary,\nand then they will be absolutely incapable of understanding higher\nmathematics. Such are the majority. Others will have this feeling only\nin a slight degree, but they will be gifted with an uncommon memory and\na great power of attention. They will learn by heart the details one\nafter another; they can understand mathematics and sometimes make\napplications, but they cannot create. Others, finally, will possess in a\nless or greater degree the special intuition referred to, and then not\nonly can they understand mathematics even if their memory is nothing\nextraordinary, but they may become creators and try to invent with more\nor less success according as this intuition is more or less developed in\nthem.\n\nIn fact, what is mathematical creation? It does not consist in making\nnew combinations with mathematical entities already known. Any one could\ndo that, but the combinations so made would be infinite in number and\nmost of them absolutely without interest. To create consists precisely\nin not making useless combinations and in making those which are useful\nand which are only a small minority. Invention is discernment, choice.\n\nHow to make this choice I have before explained; the mathematical facts\nworthy of being studied are those which, by their analogy with other\nfacts, are capable of leading us to the knowledge of a mathematical law\njust as experimental facts lead us to the knowledge of a physical law.\nThey are those which reveal to us unsuspected kinship between other\nfacts, long known, but wrongly believed to be strangers to one another.\n\nAmong chosen combinations the most fertile will often be those formed of\nelements drawn from domains which are far apart. Not that I mean as\nsufficing for invention the bringing together of objects as disparate as\npossible; most combinations so formed would be entirely sterile. But\ncertain among them, very rare, are the most fruitful of all.\n\nTo invent, I have said, is to choose; but the word is perhaps not wholly\nexact. It makes one think of a purchaser before whom are displayed a\nlarge number of samples, and who examines them, one after the other, to\nmake a choice. Here the samples would be so numerous that a whole\nlifetime would not suffice to examine them. This is not the actual state\nof things. The sterile combinations do not even present themselves to\nthe mind of the inventor. Never in the field of his consciousness do\ncombinations appear that are not really useful, except some that he\nrejects but which have to some extent the characteristics of useful\ncombinations. All goes on as if the inventor were an examiner for the\nsecond degree who would only have to question the candidates who had\npassed a previous examination.\n\nBut what I have hitherto said is what may be observed or inferred in\nreading the writings of the geometers, reading reflectively.\n\nIt is time to penetrate deeper and to see what goes on in the very soul\nof the mathematician. For this, I believe, I can do best by recalling\nmemories of my own. But I shall limit myself to telling how I wrote my\nfirst memoir on Fuchsian functions. I beg the reader's pardon; I am\nabout to use some technical expressions, but they need not frighten him,\nfor he is not obliged to understand them. I shall say, for example, that\nI have found the demonstration of such a theorem under such\ncircumstances. This theorem will have a barbarous name, unfamiliar to\nmany, but that is unimportant; what is of interest for the psychologist\nis not the theorem but the circumstances.\n\nFor fifteen days I strove to prove that there could not be any functions\nlike those I have since called Fuchsian functions. I was then very\nignorant; every day I seated myself at my work table, stayed an hour or\ntwo, tried a great number of combinations and reached no results. One\nevening, contrary to my custom, I drank black coffee and could not\nsleep. Ideas rose in crowds; I felt them collide until pairs\ninterlocked, so to speak, making a stable combination. By the next\nmorning I had established the existence of a class of Fuchsian\nfunctions, those which come from the hypergeometric series; I had only\nto write out the results, which took but a few hours.\n\nThen I wanted to represent these functions by the quotient of two\nseries; this idea was perfectly conscious and deliberate, the analogy\nwith elliptic functions guided me. I asked myself what properties these\nseries must have if they existed, and I succeeded without difficulty in\nforming the series I have called theta-Fuchsian.\n\nJust at this time I left Caen, where I was then living, to go on a\ngeologic excursion under the auspices of the school of mines. The\nchanges of travel made me forget my mathematical work. Having reached\nCoutances, we entered an omnibus to go some place or other. At the\nmoment when I put my foot on the step the idea came to me, without\nanything in my former thoughts seeming to have paved the way for it,\nthat the transformations I had used to define the Fuchsian functions\nwere identical with those of non-Euclidean geometry. I did not verify\nthe idea; I should not have had time, as, upon taking my seat in the\nomnibus, I went on with a conversation already commenced, but I felt a\nperfect certainty. On my return to Caen, for conscience' sake I verified\nthe result at my leisure.\n\nThen I turned my attention to the study of some arithmetical questions\napparently without much success and without a suspicion of any\nconnection with my preceding researches. Disgusted with my failure, I\nwent to spend a few days at the seaside, and thought of something else.\nOne morning, walking on the bluff, the idea came to me, with just the\nsame characteristics of brevity, suddenness and immediate certainty,\nthat the arithmetic transformations of indeterminate ternary quadratic\nforms were identical with those of non-Euclidean geometry.\n\nReturned to Caen, I meditated on this result and deduced the\nconsequences. The example of quadratic forms showed me that there were\nFuchsian groups other than those corresponding to the hypergeometric\nseries; I saw that I could apply to them the theory of theta-Fuchsian\nseries and that consequently there existed Fuchsian functions other than\nthose from the hypergeometric series, the ones I then knew. Naturally I\nset myself to form all these functions. I made a systematic attack upon\nthem and carried all the outworks, one after another. There was one\nhowever that still held out, whose fall would involve that of the whole\nplace. But all my efforts only served at first the better to show me the\ndifficulty, which indeed was something. All this work was perfectly\nconscious.\n\nThereupon I left for Mont-Val\u00e9rien, where I was to go through my\nmilitary service; so I was very differently occupied. One day, going\nalong the street, the solution of the difficulty which had stopped me\nsuddenly appeared to me. I did not try to go deep into it immediately,\nand only after my service did I again take up the question. I had all\nthe elements and had only to arrange them and put them together. So I\nwrote out my final memoir at a single stroke and without difficulty.\n\nI shall limit myself to this single example; it is useless to multiply\nthem. In regard to my other researches I would have to say analogous\nthings, and the observations of other mathematicians given in\n_L'enseignement math\u00e9matique_ would only confirm them.\n\nMost striking at first is this appearance of sudden illumination, a\nmanifest sign of long, unconscious prior work. The r\u00f4le of this\nunconscious work in mathematical invention appears to me incontestable,\nand traces of it would be found in other cases where it is less evident.\nOften when one works at a hard question, nothing good is accomplished at\nthe first attack. Then one takes a rest, longer or shorter, and sits\ndown anew to the work. During the first half-hour, as before, nothing is\nfound, and then all of a sudden the decisive idea presents itself to the\nmind. It might be said that the conscious work has been more fruitful\nbecause it has been interrupted and the rest has given back to the mind\nits force and freshness. But it is more probable that this rest has been\nfilled out with unconscious work and that the result of this work has\nafterward revealed itself to the geometer just as in the cases I have\ncited; only the revelation, instead of coming during a walk or a\njourney, has happened during a period of conscious work, but\nindependently of this work which plays at most a r\u00f4le of excitant, as if\nit were the goad stimulating the results already reached during rest,\nbut remaining unconscious, to assume the conscious form.\n\nThere is another remark to be made about the conditions of this\nunconscious work: it is possible, and of a certainty it is only\nfruitful, if it is on the one hand preceded and on the other hand\nfollowed by a period of conscious work. These sudden inspirations (and\nthe examples already cited sufficiently prove this) never happen except\nafter some days of voluntary effort which has appeared absolutely\nfruitless and whence nothing good seems to have come, where the way\ntaken seems totally astray. These efforts then have not been as sterile\nas one thinks; they have set agoing the unconscious machine and without\nthem it would not have moved and would have produced nothing.\n\nThe need for the second period of conscious work, after the inspiration,\nis still easier to understand. It is necessary to put in shape the\nresults of this inspiration, to deduce from them the immediate\nconsequences, to arrange them, to word the demonstrations, but above all\nis verification necessary. I have spoken of the feeling of absolute\ncertitude accompanying the inspiration; in the cases cited this feeling\nwas no deceiver, nor is it usually. But do not think this a rule without\nexception; often this feeling deceives us without being any the less\nvivid, and we only find it out when we seek to put on foot the\ndemonstration. I have especially noticed this fact in regard to ideas\ncoming to me in the morning or evening in bed while in a semi-hypnagogic\nstate.\n\nSuch are the realities; now for the thoughts they force upon us. The\nunconscious, or, as we say, the subliminal self plays an important r\u00f4le\nin mathematical creation; this follows from what we have said. But\nusually the subliminal self is considered as purely automatic. Now we\nhave seen that mathematical work is not simply mechanical, that it could\nnot be done by a machine, however perfect. It is not merely a question\nof applying rules, of making the most combinations possible according to\ncertain fixed laws. The combinations so obtained would be exceedingly\nnumerous, useless and cumbersome. The true work of the inventor consists\nin choosing among these combinations so as to eliminate the useless ones\nor rather to avoid the trouble of making them, and the rules which must\nguide this choice are extremely fine and delicate. It is almost\nimpossible to state them precisely; they are felt rather than\nformulated. Under these conditions, how imagine a sieve capable of\napplying them mechanically?\n\nA first hypothesis now presents itself: the subliminal self is in no way\ninferior to the conscious self; it is not purely automatic; it is\ncapable of discernment; it has tact, delicacy; it knows how to choose,\nto divine. What do I say? It knows better how to divine than the\nconscious self, since it succeeds where that has failed. In a word, is\nnot the subliminal self superior to the conscious self? You recognize\nthe full importance of this question. Boutroux in a recent lecture has\nshown how it came up on a very different occasion, and what consequences\nwould follow an affirmative answer. (See also, by the same author,\n_Science et Religion_, pp. 313 ff.)\n\nIs this affirmative answer forced upon us by the facts I have just\ngiven? I confess that, for my part, I should hate to accept it.\nReexamine the facts then and see if they are not compatible with another\nexplanation.\n\nIt is certain that the combinations which present themselves to the mind\nin a sort of sudden illumination, after an unconscious working somewhat\nprolonged, are generally useful and fertile combinations, which seem the\nresult of a first impression. Does it follow that the subliminal self,\nhaving divined by a delicate intuition that these combinations would be\nuseful, has formed only these, or has it rather formed many others which\nwere lacking in interest and have remained unconscious?\n\nIn this second way of looking at it, all the combinations would be\nformed in consequence of the automatism of the subliminal self, but only\nthe interesting ones would break into the domain of consciousness. And\nthis is still very mysterious. What is the cause that, among the\nthousand products of our unconscious activity, some are called to pass\nthe threshold, while others remain below? Is it a simple chance which\nconfers this privilege? Evidently not; among all the stimuli of our\nsenses, for example, only the most intense fix our attention, unless it\nhas been drawn to them by other causes. More generally the privileged\nunconscious phenomena, those susceptible of becoming conscious, are\nthose which, directly or indirectly, affect most profoundly our\nemotional sensibility.\n\nIt may be surprising to see emotional sensibility invoked _\u00e0 propos_ of\nmathematical demonstrations which, it would seem, can interest only the\nintellect. This would be to forget the feeling of mathematical beauty,\nof the harmony of numbers and forms, of geometric elegance. This is a\ntrue esthetic feeling that all real mathematicians know, and surely it\nbelongs to emotional sensibility.\n\nNow, what are the mathematic entities to which we attribute this\ncharacter of beauty and elegance, and which are capable of developing in\nus a sort of esthetic emotion? They are those whose elements are\nharmoniously disposed so that the mind without effort can embrace their\ntotality while realizing the details. This harmony is at once a\nsatisfaction of our esthetic needs and an aid to the mind, sustaining\nand guiding; And at the same time, in putting under our eyes a\nwell-ordered whole, it makes us foresee a mathematical law. Now, as we\nhave said above, the only mathematical facts worthy of fixing our\nattention and capable of being useful are those which can teach us a\nmathematical law. So that we reach the following conclusion: The useful\ncombinations are precisely the most beautiful, I mean those best able to\ncharm this special sensibility that all mathematicians know, but of\nwhich the profane are so ignorant as often to be tempted to smile at it.\n\nWhat happens then? Among the great numbers of combinations blindly\nformed by the subliminal self, almost all are without interest and\nwithout utility; but just for that reason they are also without effect\nupon the esthetic sensibility. Consciousness will never know them; only\ncertain ones are harmonious, and, consequently, at once useful and\nbeautiful. They will be capable of touching this special sensibility of\nthe geometer of which I have just spoken, and which, once aroused, will\ncall our attention to them, and thus give them occasion to become\nconscious.\n\nThis is only a hypothesis, and yet here is an observation which may\nconfirm it: when a sudden illumination seizes upon the mind of the\nmathematician, it usually happens that it does not deceive him, but it\nalso sometimes happens, as I have said, that it does not stand the test\nof verification; well, we almost always notice that this false idea, had\nit been true, would have gratified our natural feeling for mathematical\nelegance.\n\nThus it is this special esthetic sensibility which plays the r\u00f4le of the\ndelicate sieve of which I spoke, and that sufficiently explains why the\none lacking it will never be a real creator.\n\nYet all the difficulties have not disappeared. The conscious self is\nnarrowly limited, and as for the subliminal self we know not its\nlimitations, and this is why we are not too reluctant in supposing that\nit has been able in a short time to make more different combinations\nthan the whole life of a conscious being could encompass. Yet these\nlimitations exist. Is it likely that it is able to form all the possible\ncombinations, whose number would frighten the imagination? Nevertheless\nthat would seem necessary, because if it produces only a small part of\nthese combinations, and if it makes them at random, there would be\nsmall chance that the _good_, the one we should choose, would be found\namong them.\n\nPerhaps we ought to seek the explanation in that preliminary period of\nconscious work which always precedes all fruitful unconscious labor.\nPermit me a rough comparison. Figure the future elements of our\ncombinations as something like the hooked atoms of Epicurus. During the\ncomplete repose of the mind, these atoms are motionless, they are, so to\nspeak, hooked to the wall; so this complete rest may be indefinitely\nprolonged without the atoms meeting, and consequently without any\ncombination between them.\n\nOn the other hand, during a period of apparent rest and unconscious\nwork, certain of them are detached from the wall and put in motion. They\nflash in every direction through the space (I was about to say the room)\nwhere they are enclosed, as would, for example, a swarm of gnats or, if\nyou prefer a more learned comparison, like the molecules of gas in the\nkinematic theory of gases. Then their mutual impacts may produce new\ncombinations.\n\nWhat is the r\u00f4le of the preliminary conscious work? It is evidently to\nmobilize certain of these atoms, to unhook them from the wall and put\nthem in swing. We think we have done no good, because we have moved\nthese elements a thousand different ways in seeking to assemble them,\nand have found no satisfactory aggregate. But, after this shaking up\nimposed upon them by our will, these atoms do not return to their\nprimitive rest. They freely continue their dance.\n\nNow, our will did not choose them at random; it pursued a perfectly\ndetermined aim. The mobilized atoms are therefore not any atoms\nwhatsoever; they are those from which we might reasonably expect the\ndesired solution. Then the mobilized atoms undergo impacts which make\nthem enter into combinations among themselves or with other atoms at\nrest which they struck against in their course. Again I beg pardon, my\ncomparison is very rough, but I scarcely know how otherwise to make my\nthought understood.\n\nHowever it may be, the only combinations that have a chance of forming\nare those where at least one of the elements is one of those atoms\nfreely chosen by our will. Now, it is evidently among these that is\nfound what I called the _good combination_. Perhaps this is a way of\nlessening the paradoxical in the original hypothesis.\n\nAnother observation. It never happens that the unconscious work gives us\nthe result of a somewhat long calculation _all made_, where we have only\nto apply fixed rules. We might think the wholly automatic subliminal\nself particularly apt for this sort of work, which is in a way\nexclusively mechanical. It seems that thinking in the evening upon the\nfactors of a multiplication we might hope to find the product ready made\nupon our awakening, or again that an algebraic calculation, for example\na verification, would be made unconsciously. Nothing of the sort, as\nobservation proves. All one may hope from these inspirations, fruits of\nunconscious work, is a point of departure for such calculations. As for\nthe calculations themselves, they must be made in the second period of\nconscious work, that which follows the inspiration, that in which one\nverifies the results of this inspiration and deduces their consequences.\nThe rules of these calculations are strict and complicated. They require\ndiscipline, attention, will, and therefore consciousness. In the\nsubliminal self, on the contrary, reigns what I should call liberty, if\nwe might give this name to the simple absence of discipline and to the\ndisorder born of chance. Only, this disorder itself permits unexpected\ncombinations.\n\nI shall make a last remark: when above I made certain personal\nobservations, I spoke of a night of excitement when I worked in spite of\nmyself. Such cases are frequent, and it is not necessary that the\nabnormal cerebral activity be caused by a physical excitant as in that I\nmentioned. It seems, in such cases, that one is present at his own\nunconscious work, made partially perceptible to the over-excited\nconsciousness, yet without having changed its nature. Then we vaguely\ncomprehend what distinguishes the two mechanisms or, if you wish, the\nworking methods of the two egos. And the psychologic observations I have\nbeen able thus to make seem to me to confirm in their general outlines\nthe views I have given.\n\nSurely they have need of it, for they are and remain in spite of all\nvery hypothetical: the interest of the questions is so great that I do\nnot repent of having submitted them to the reader.\n\n\n\n\nCHAPTER IV\n\nCHANCE\n\n\nI\n\n\"How dare we speak of the laws of chance? Is not chance the antithesis\nof all law?\" So says Bertrand at the beginning of his _Calcul des\nprobabiltit\u00e9s_. Probability is opposed to certitude; so it is what we do\nnot know and consequently it seems what we could not calculate. Here is\nat least apparently a contradiction, and about it much has already been\nwritten.\n\nAnd first, what is chance? The ancients distinguished between phenomena\nseemingly obeying harmonious laws, established once for all, and those\nwhich they attributed to chance; these were the ones unpredictable\nbecause rebellious to all law. In each domain the precise laws did not\ndecide everything, they only drew limits between which chance might act.\nIn this conception the word chance had a precise and objective meaning;\nwhat was chance for one was also chance for another and even for the\ngods.\n\nBut this conception is not ours to-day. We have become absolute\ndeterminists, and even those who want to reserve the rights of human\nfree will let determinism reign undividedly in the inorganic world at\nleast. Every phenomenon, however minute, has a cause; and a mind\ninfinitely powerful, infinitely well-informed about the laws of nature,\ncould have foreseen it from the beginning of the centuries. If such a\nmind existed, we could not play with it at any game of chance; we should\nalways lose.\n\nIn fact for it the word chance would not have any meaning, or rather\nthere would be no chance. It is because of our weakness and our\nignorance that the word has a meaning for us. And, even without going\nbeyond our feeble humanity, what is chance for the ignorant is not\nchance for the scientist. Chance is only the measure of our ignorance.\nFortuitous phenomena are, by definition, those whose laws we do not\nknow.\n\nBut is this definition altogether satisfactory? When the first Chaldean\nshepherds followed with their eyes the movements of the stars, they knew\nnot as yet the laws of astronomy; would they have dreamed of saying that\nthe stars move at random? If a modern physicist studies a new\nphenomenon, and if he discovers its law Tuesday, would he have said\nMonday that this phenomenon was fortuitous? Moreover, do we not often\ninvoke what Bertrand calls the laws of chance, to predict a phenomenon?\nFor example, in the kinetic theory of gases we obtain the known laws of\nMariotte and of Gay-Lussac by means of the hypothesis that the\nvelocities of the molecules of gas vary irregularly, that is to say at\nrandom. All physicists will agree that the observable laws would be much\nless simple if the velocities were ruled by any simple elementary law\nwhatsoever, if the molecules were, as we say, _organized_, if they were\nsubject to some discipline. It is due to chance, that is to say, to our\nignorance, that we can draw our conclusions; and then if the word chance\nis simply synonymous with ignorance what does that mean? Must we\ntherefore translate as follows?\n\n\"You ask me to predict for you the phenomena about to happen. If,\nunluckily, I knew the laws of these phenomena I could make the\nprediction only by inextricable calculations and would have to renounce\nattempting to answer you; but as I have the good fortune not to know\nthem, I will answer you at once. And what is most surprising, my answer\nwill be right.\"\n\nSo it must well be that chance is something other than the name we give\nour ignorance, that among phenomena whose causes are unknown to us we\nmust distinguish fortuitous phenomena about which the calculus of\nprobabilities will provisionally give information, from those which are\nnot fortuitous and of which we can say nothing so long as we shall not\nhave determined the laws governing them. For the fortuitous phenomena\nthemselves, it is clear that the information given us by the calculus of\nprobabilities will not cease to be true upon the day when these\nphenomena shall be better known.\n\nThe director of a life insurance company does not know when each of the\ninsured will die, but he relies upon the calculus of probabilities and\non the law of great numbers, and he is not deceived, since he\ndistributes dividends to his stockholders. These dividends would not\nvanish if a very penetrating and very indiscreet physician should, after\nthe policies were signed, reveal to the director the life chances of the\ninsured. This doctor would dissipate the ignorance of the director, but\nhe would have no influence on the dividends, which evidently are not an\noutcome of this ignorance.\n\n\nII\n\nTo find a better definition of chance we must examine some of the facts\nwhich we agree to regard as fortuitous, and to which the calculus of\nprobabilities seems to apply; we then shall investigate what are their\ncommon characteristics.\n\nThe first example we select is that of unstable equilibrium; if a cone\nrests upon its apex, we know well that it will fall, but we do not know\ntoward what side; it seems to us chance alone will decide. If the cone\nwere perfectly symmetric, if its axis were perfectly vertical, if it\nwere acted upon by no force other than gravity, it would not fall at\nall. But the least defect in symmetry will make it lean slightly toward\none side or the other, and if it leans, however little, it will fall\naltogether toward that side. Even if the symmetry were perfect, a very\nslight tremor, a breath of air could make it incline some seconds of\narc; this will be enough to determine its fall and even the sense of its\nfall which will be that of the initial inclination.\n\nA very slight cause, which escapes us, determines a considerable effect\nwhich we can not help seeing, and then we say this effect is due to\nchance. If we could know exactly the laws of nature and the situation of\nthe universe at the initial instant, we should be able to predict\nexactly the situation of this same universe at a subsequent instant. But\neven when the natural laws should have no further secret for us, we\ncould know the initial situation only _approximately_. If that permits\nus to foresee the subsequent situation _with the same degree of\napproximation_, this is all we require, we say the phenomenon has been\npredicted, that it is ruled by laws. But this is not always the case; it\nmay happen that slight differences in the initial conditions produce\nvery great differences in the final phenomena; a slight error in the\nformer would make an enormous error in the latter. Prediction becomes\nimpossible and we have the fortuitous phenomenon.\n\nOur second example will be very analogous to the first and we shall take\nit from meteorology. Why have the meteorologists such difficulty in\npredicting the weather with any certainty? Why do the rains, the\ntempests themselves seem to us to come by chance, so that many persons\nfind it quite natural to pray for rain or shine, when they would think\nit ridiculous to pray for an eclipse? We see that great perturbations\ngenerally happen in regions where the atmosphere is in unstable\nequilibrium. The meteorologists are aware that this equilibrium is\nunstable, that a cyclone is arising somewhere; but where they can not\ntell; one-tenth of a degree more or less at any point, and the cyclone\nbursts here and not there, and spreads its ravages over countries it\nwould have spared. This we could have foreseen if we had known that\ntenth of a degree, but the observations were neither sufficiently close\nnor sufficiently precise, and for this reason all seems due to the\nagency of chance. Here again we find the same contrast between a very\nslight cause, unappreciable to the observer, and important effects,\nwhich are sometimes tremendous disasters.\n\nLet us pass to another example, the distribution of the minor planets on\nthe zodiac. Their initial longitudes may have been any longitudes\nwhatever; but their mean motions were different and they have revolved\nfor so long a time that we may say they are now distributed _at random_\nalong the zodiac. Very slight initial differences between their\ndistances from the sun, or, what comes to the same thing, between their\nmean motions, have ended by giving enormous differences between their\npresent longitudes. An excess of the thousandth of a second in the daily\nmean motion will give in fact a second in three years, a degree in ten\nthousand years, an entire circumference in three or four million years,\nand what is that to the time which has passed since the minor planets\ndetached themselves from the nebula of Laplace? Again therefore we see a\nslight cause and a great effect; or better, slight differences in the\ncause and great differences in the effect.\n\nThe game of roulette does not take us as far as might seem from the\npreceding example. Assume a needle to be turned on a pivot over a dial\ndivided into a hundred sectors alternately red and black. If it stops on\na red sector I win; if not, I lose. Evidently all depends upon the\ninitial impulse I give the needle. The needle will make, suppose, ten or\ntwenty turns, but it will stop sooner or not so soon, according as I\nshall have pushed it more or less strongly. It suffices that the impulse\nvary only by a thousandth or a two thousandth to make the needle stop\nover a black sector or over the following red one. These are differences\nthe muscular sense can not distinguish and which elude even the most\ndelicate instruments. So it is impossible for me to foresee what the\nneedle I have started will do, and this is why my heart throbs and I\nhope everything from luck. The difference in the cause is imperceptible,\nand the difference in the effect is for me of the highest importance,\nsince it means my whole stake.\n\n\nIII\n\nPermit me, in this connection, a thought somewhat foreign to my subject.\nSome years ago a philosopher said that the future is determined by the\npast, but not the past by the future; or, in other words, from knowledge\nof the present we could deduce the future, but not the past; because,\nsaid he, a cause can have only one effect, while the same effect might\nbe produced by several different causes. It is clear no scientist can\nsubscribe to this conclusion. The laws of nature bind the antecedent to\nthe consequent in such a way that the antecedent is as well determined\nby the consequent as the consequent by the antecedent. But whence came\nthe error of this philosopher? We know that in virtue of Carnot's\nprinciple physical phenomena are irreversible and the world tends toward\nuniformity. When two bodies of different temperature come in contact,\nthe warmer gives up heat to the colder; so we may foresee that the\ntemperature will equalize. But once equal, if asked about the anterior\nstate, what can we answer? We might say that one was warm and the other\ncold, but not be able to divine which formerly was the warmer.\n\nAnd yet in reality the temperatures will never reach perfect equality.\nThe difference of the temperatures only tends asymptotically toward\nzero. There comes a moment when our thermometers are powerless to make\nit known. But if we had thermometers a thousand times, a hundred\nthousand times as sensitive, we should recognize that there still is a\nslight difference, and that one of the bodies remains a little warmer\nthan the other, and so we could say this it is which formerly was much\nthe warmer.\n\nSo then there are, contrary to what we found in the former examples,\ngreat differences in cause and slight differences in effect. Flammarion\nonce imagined an observer going away from the earth with a velocity\ngreater than that of light; for him time would have changed sign.\nHistory would be turned about, and Waterloo would precede Austerlitz.\nWell, for this observer, effects and causes would be inverted; unstable\nequilibrium would no longer be the exception. Because of the universal\nirreversibility, all would seem to him to come out of a sort of chaos in\nunstable equilibrium. All nature would appear to him delivered over to\nchance.\n\n\nIV\n\nNow for other examples where we shall see somewhat different\ncharacteristics. Take first the kinetic theory of gases. How should we\npicture a receptacle filled with gas? Innumerable molecules, moving at\nhigh speeds, flash through this receptacle in every direction. At every\ninstant they strike against its walls or each other, and these\ncollisions happen under the most diverse conditions. What above all\nimpresses us here is not the littleness of the causes, but their\ncomplexity, and yet the former element is still found here and plays an\nimportant r\u00f4le. If a molecule deviated right or left from its\ntrajectory, by a very small quantity, comparable to the radius of action\nof the gaseous molecules, it would avoid a collision or sustain it under\ndifferent conditions, and that would vary the direction of its velocity\nafter the impact, perhaps by ninety degrees or by a hundred and eighty\ndegrees.\n\nAnd this is not all; we have just seen that it is necessary to deflect\nthe molecule before the clash by only an infinitesimal, to produce its\ndeviation after the collision by a finite quantity. If then the molecule\nundergoes two successive shocks, it will suffice to deflect it before\nthe first by an infinitesimal of the second order, for it to deviate\nafter the first encounter by an infinitesimal of the first order, and\nafter the second hit, by a finite quantity. And the molecule will not\nundergo merely two shocks; it will undergo a very great number per\nsecond. So that if the first shock has multiplied the deviation by a\nvery large number _A_, after _n_ shocks it will be multiplied by\n_A_^{_n_}. It will therefore become very great not merely because _A_\nis large, that is to say because little causes produce big effects, but\nbecause the exponent _n_ is large, that is to say because the shocks are\nvery numerous and the causes very complex.\n\nTake a second example. Why do the drops of rain in a shower seem to be\ndistributed at random? This is again because of the complexity of the\ncauses which determine their formation. Ions are distributed in the\natmosphere. For a long while they have been subjected to air-currents\nconstantly changing, they have been caught in very small whirlwinds, so\nthat their final distribution has no longer any relation to their\ninitial distribution. Suddenly the temperature falls, vapor condenses,\nand each of these ions becomes the center of a drop of rain. To know\nwhat will be the distribution of these drops and how many will fall on\neach paving-stone, it would not be sufficient to know the initial\nsituation of the ions, it would be necessary to compute the effect of a\nthousand little capricious air-currents.\n\nAnd again it is the same if we put grains of powder in suspension in\nwater. The vase is ploughed by currents whose law we know not, we only\nknow it is very complicated. At the end of a certain time the grains\nwill be distributed at random, that is to say uniformly, in the vase;\nand this is due precisely to the complexity of these currents. If they\nobeyed some simple law, if for example the vase revolved and the\ncurrents circulated around the axis of the vase, describing circles, it\nwould no longer be the same, since each grain would retain its initial\naltitude and its initial distance from the axis.\n\nWe should reach the same result in considering the mixing of two liquids\nor of two fine-grained powders. And to take a grosser example, this is\nalso what happens when we shuffle playing-cards. At each stroke the\ncards undergo a permutation (analogous to that studied in the theory of\nsubstitutions). What will happen? The probability of a particular\npermutation (for example, that bringing to the _n_th place the card\noccupying the [phi](_n_)th place before the permutation) depends upon\nthe player's habits. But if this player shuffles the cards long enough,\nthere will be a great number of successive permutations, and the\nresulting final order will no longer be governed by aught but chance; I\nmean to say that all possible orders will be equally probable. It is to\nthe great number of successive permutations, that is to say to the\ncomplexity of the phenomenon, that this result is due.\n\nA final word about the theory of errors. Here it is that the causes are\ncomplex and multiple. To how many snares is not the observer exposed,\neven with the best instrument! He should apply himself to finding out\nthe largest and avoiding them. These are the ones giving birth to\nsystematic errors. But when he has eliminated those, admitting that he\nsucceeds, there remain many small ones which, their effects\naccumulating, may become dangerous. Thence come the accidental errors;\nand we attribute them to chance because their causes are too complicated\nand too numerous. Here again we have only little causes, but each of\nthem would produce only a slight effect; it is by their union and their\nnumber that their effects become formidable.\n\n\nV\n\nWe may take still a third point of view, less important than the first\ntwo and upon which I shall lay less stress. When we seek to foresee an\nevent and examine its antecedents, we strive to search into the anterior\nsituation. This could not be done for all parts of the universe and we\nare content to know what is passing in the neighborhood of the point\nwhere the event should occur, or what would appear to have some relation\nto it. An examination can not be complete and we must know how to\nchoose. But it may happen that we have passed by circumstances which at\nfirst sight seemed completely foreign to the foreseen happening, to\nwhich one would never have dreamed of attributing any influence and\nwhich nevertheless, contrary to all anticipation, come to play an\nimportant r\u00f4le.\n\nA man passes in the street going to his business; some one knowing the\nbusiness could have told why he started at such a time and went by such\na street. On the roof works a tiler. The contractor employing him could\nin a certain measure foresee what he would do. But the passer-by\nscarcely thinks of the tiler, nor the tiler of him; they seem to belong\nto two worlds completely foreign to one another. And yet the tiler drops\na tile which kills the man, and we do not hesitate to say this is\nchance.\n\nOur weakness forbids our considering the entire universe and makes us\ncut it up into slices. We try to do this as little artificially as\npossible. And yet it happens from time to time that two of these slices\nreact upon each other. The effects of this mutual action then seem to us\nto be due to chance.\n\nIs this a third way of conceiving chance? Not always; in fact most often\nwe are carried back to the first or the second. Whenever two worlds\nusually foreign to one another come thus to react upon each other, the\nlaws of this reaction must be very complex. On the other hand, a very\nslight change in the initial conditions of these two worlds would have\nbeen sufficient for the reaction not to have happened. How little was\nneeded for the man to pass a second later or the tiler to drop his tile\na second sooner.\n\n\nVI\n\nAll we have said still does not explain why chance obeys laws. Does the\nfact that the causes are slight or complex suffice for our foreseeing,\nif not their effects _in each case_, at least what their effects will\nbe, _on the average_? To answer this question we had better take up\nagain some of the examples already cited.\n\nI shall begin with that of the roulette. I have said that the point\nwhere the needle will stop depends upon the initial push given it. What\nis the probability of this push having this or that value? I know\nnothing about it, but it is difficult for me not to suppose that this\nprobability is represented by a continuous analytic function. The\nprobability that the push is comprised between [alpha] and [alpha] +\n[epsilon] will then be sensibly equal to the probability of its being\ncomprised between [alpha] + [epsilon] and [alpha] + 2[epsilon],\n_provided_ [epsilon] _be very small_. This is a property common to all\nanalytic functions. Minute variations of the function are proportional\nto minute variations of the variable.\n\nBut we have assumed that an exceedingly slight variation of the push\nsuffices to change the color of the sector over which the needle finally\nstops. From [alpha] to [alpha]+[epsilon] it is red, from\n[alpha]+[epsilon] to [alpha]+2[epsilon] it is black; the probability of\neach red sector is therefore the same as of the following black, and\nconsequently the total probability of red equals the total probability\nof black.\n\nThe datum of the question is the analytic function representing the\nprobability of a particular initial push. But the theorem remains true\nwhatever be this datum, since it depends upon a property common to all\nanalytic functions. From this it follows finally that we no longer need\nthe datum.\n\nWhat we have just said for the case of the roulette applies also to the\nexample of the minor planets. The zodiac may be regarded as an immense\nroulette on which have been tossed many little balls with different\ninitial impulses varying according to some law. Their present\ndistribution is uniform and independent of this law, for the same reason\nas in the preceding case. Thus we see why phenomena obey the laws of\nchance when slight differences in the causes suffice to bring on great\ndifferences in the effects. The probabilities of these slight\ndifferences may then be regarded as proportional to these differences\nthemselves, just because these differences are minute, and the\ninfinitesimal increments of a continuous function are proportional to\nthose of the variable.\n\nTake an entirely different example, where intervenes especially the\ncomplexity of the causes. Suppose a player shuffles a pack of cards. At\neach shuffle he changes the order of the cards, and he may change them\nin many ways. To simplify the exposition, consider only three cards. The\ncards which before the shuffle occupied respectively the places 123, may\nafter the shuffle occupy the places\n\n 123, 231, 312, 321, 132, 213.\n\nEach of these six hypotheses is possible and they have respectively for\nprobabilities:\n\n p_1, p_2, p_3, p_4, p_5, p_6.\n\nThe sum of these six numbers equals 1; but this is all we know of them;\nthese six probabilities depend naturally upon the habits of the player\nwhich we do not know.\n\nAt the second shuffle and the following, this will recommence, and under\nthe same conditions; I mean that p_4 for example represents always the\nprobability that the three cards which occupied after the _n_th shuffle\nand before the _n_ + 1th the places 123, occupy the places 321 after the\n_n_ + 1th shuffle. And this remains true whatever be the number _n_,\nsince the habits of the player and his way of shuffling remain the same.\n\nBut if the number of shuffles is very great, the cards which before the\nfirst shuffle occupied the places 123 may, after the last shuffle,\noccupy the places\n\n 123, 231, 312, 321, 132, 213\n\nand the probability of these six hypotheses will be sensibly the same\nand equal to 1/6; and this will be true whatever be the numbers\np_1 ... p_6 which we do not know. The great number of shuffles, that\nis to say the complexity of the causes, has produced uniformity.\n\nThis would apply without change if there were more than three cards,\nbut even with three cards the demonstration would be complicated;\nlet it suffice to give it for only two cards. Then we have only two\npossibilities 12, 21 with the probabilities p_1 and p_2 = 1 - p_1.\n\nSuppose _n_ shuffles and suppose I win one franc if the cards are\nfinally in the initial order and lose one if they are finally inverted.\nThen, my mathematical expectation will be (p_1 - p_2)^{_n_}.\n\nThe difference p_1 - p_2 is certainly less than 1; so that if _n_ is\nvery great my expectation will be zero; we need not learn p_1 and p_2\nto be aware that the game is equitable.\n\nThere would always be an exception if one of the numbers p_1 and p_2\nwas equal to 1 and the other naught. _Then it would not apply because\nour initial hypotheses would be too simple._\n\nWhat we have just seen applies not only to the mixing of cards, but to\nall mixings, to those of powders and of liquids; and even to those of\nthe molecules of gases in the kinetic theory of gases.\n\nTo return to this theory, suppose for a moment a gas whose molecules can\nnot mutually clash, but may be deviated by hitting the insides of the\nvase wherein the gas is confined. If the form of the vase is\nsufficiently complex the distribution of the molecules and that of the\nvelocities will not be long in becoming uniform. But this will not be so\nif the vase is spherical or if it has the shape of a cuboid. Why?\nBecause in the first case the distance from the center to any trajectory\nwill remain constant; in the second case this will be the absolute value\nof the angle of each trajectory with the faces of the cuboid.\n\nSo we see what should be understood by conditions _too simple_; they are\nthose which conserve something, which leave an invariant remaining. Are\nthe differential equations of the problem too simple for us to apply the\nlaws of chance? This question would seem at first view to lack precise\nmeaning; now we know what it means. They are too simple if they conserve\nsomething, if they admit a uniform integral. If something in the initial\nconditions remains unchanged, it is clear the final situation can no\nlonger be independent of the initial situation.\n\nWe come finally to the theory of errors. We know not to what are due the\naccidental errors, and precisely because we do not know, we are aware\nthey obey the law of Gauss. Such is the paradox. The explanation is\nnearly the same as in the preceding cases. We need know only one thing:\nthat the errors are very numerous, that they are very slight, that each\nmay be as well negative as positive. What is the curve of probability of\neach of them? We do not know; we only suppose it is symmetric. We prove\nthen that the resultant error will follow Gauss's law, and this\nresulting law is independent of the particular laws which we do not\nknow. Here again the simplicity of the result is born of the very\ncomplexity of the data.\n\n\nVII\n\nBut we are not through with paradoxes. I have just recalled the figment\nof Flammarion, that of the man going quicker than light, for whom time\nchanges sign. I said that for him all phenomena would seem due to\nchance. That is true from a certain point of view, and yet all these\nphenomena at a given moment would not be distributed in conformity with\nthe laws of chance, since the distribution would be the same as for us,\nwho, seeing them unfold harmoniously and without coming out of a primal\nchaos, do not regard them as ruled by chance.\n\nWhat does that mean? For Lumen, Flammarion's man, slight causes seem to\nproduce great effects; why do not things go on as for us when we think\nwe see grand effects due to little causes? Would not the same reasoning\nbe applicable in his case?\n\nLet us return to the argument. When slight differences in the causes\nproduce vast differences in the effects, why are these effects\ndistributed according to the laws of chance? Suppose a difference of a\nmillimeter in the cause produces a difference of a kilometer in the\neffect. If I win in case the effect corresponds to a kilometer bearing\nan even number, my probability of winning will be 1/2. Why? Because to\nmake that, the cause must correspond to a millimeter with an even\nnumber. Now, according to all appearance, the probability of the cause\nvarying between certain limits will be proportional to the distance\napart of these limits, provided this distance be very small. If this\nhypothesis were not admitted there would no longer be any way of\nrepresenting the probability by a continuous function.\n\nWhat now will happen when great causes produce small effects? This is\nthe case where we should not attribute the phenomenon to chance and\nwhere on the contrary Lumen would attribute it to chance. To a\ndifference of a kilometer in the cause would correspond a difference of\na millimeter in the effect. Would the probability of the cause being\ncomprised between two limits _n_ kilometers apart still be proportional\nto _n_? We have no reason to suppose so, since this distance, _n_\nkilometers, is great. But the probability that the effect lies between\ntwo limits _n_ millimeters apart will be precisely the same, so it will\nnot be proportional to _n_, even though this distance, _n_ millimeters,\nbe small. There is no way therefore of representing the law of\nprobability of effects by a continuous curve. This curve, understand,\nmay remain continuous in the _analytic_ sense of the word; to\n_infinitesimal_ variations of the abscissa will correspond infinitesimal\nvariations of the ordinate. But _practically_ it will not be continuous,\nsince _very small_ variations of the ordinate would not correspond to\nvery small variations of the abscissa. It would become impossible to\ntrace the curve with an ordinary pencil; that is what I mean.\n\nSo what must we conclude? Lumen has no right to say that the\nprobability of the cause (_his_ cause, our effect) should be represented\nnecessarily by a continuous function. But then why have we this right?\nIt is because this state of unstable equilibrium which we have been\ncalling initial is itself only the final outcome of a long previous\nhistory. In the course of this history complex causes have worked a\ngreat while: they have contributed to produce the mixture of elements\nand they have tended to make everything uniform at least within a small\nregion; they have rounded off the corners, smoothed down the hills and\nfilled up the valleys. However capricious and irregular may have been\nthe primitive curve given over to them, they have worked so much toward\nmaking it regular that finally they deliver over to us a continuous\ncurve. And this is why we may in all confidence assume its continuity.\n\nLumen would not have the same reasons for such a conclusion. For him\ncomplex causes would not seem agents of equalization and regularity, but\non the contrary would create only inequality and differentiation. He\nwould see a world more and more varied come forth from a sort of\nprimitive chaos. The changes he could observe would be for him\nunforeseen and impossible to foresee. They would seem to him due to some\ncaprice or another; but this caprice would be quite different from our\nchance, since it would be opposed to all law, while our chance still has\nits laws. All these points call for lengthy explications, which perhaps\nwould aid in the better comprehension of the irreversibility of the\nuniverse.\n\n\nVIII\n\nWe have sought to define chance, and now it is proper to put a question.\nHas chance thus defined, in so far as this is possible, objectivity?\n\nIt may be questioned. I have spoken of very slight or very complex\ncauses. But what is very little for one may be very big for another, and\nwhat seems very complex to one may seem simple to another. In part I\nhave already answered by saying precisely in what cases differential\nequations become too simple for the laws of chance to remain applicable.\nBut it is fitting to examine the matter a little more closely, because\nwe may take still other points of view.\n\nWhat means the phrase 'very slight'? To understand it we need only go\nback to what has already been said. A difference is very slight, an\ninterval is very small, when within the limits of this interval the\nprobability remains sensibly constant. And why may this probability be\nregarded as constant within a small interval? It is because we assume\nthat the law of probability is represented by a continuous curve,\ncontinuous not only in the analytic sense, but _practically_ continuous,\nas already explained. This means that it not only presents no absolute\nhiatus, but that it has neither salients nor reentrants too acute or too\naccentuated.\n\nAnd what gives us the right to make this hypothesis? We have already\nsaid it is because, since the beginning of the ages, there have always\nbeen complex causes ceaselessly acting in the same way and making the\nworld tend toward uniformity without ever being able to turn back. These\nare the causes which little by little have flattened the salients and\nfilled up the reentrants, and this is why our probability curves now\nshow only gentle undulations. In milliards of milliards of ages another\nstep will have been made toward uniformity, and these undulations will\nbe ten times as gentle; the radius of mean curvature of our curve will\nhave become ten times as great. And then such a length as seems to us\nto-day not very small, since on our curve an arc of this length can not\nbe regarded as rectilineal, should on the contrary at that epoch be\ncalled very little, since the curvature will have become ten times less\nand an arc of this length may be sensibly identified with a sect.\n\nThus the phrase 'very slight' remains relative; but it is not relative\nto such or such a man, it is relative to the actual state of the world.\nIt will change its meaning when the world shall have become more\nuniform, when all things shall have blended still more. But then\ndoubtless men can no longer live and must give place to other\nbeings--should I say far smaller or far larger? So that our criterion,\nremaining true for all men, retains an objective sense.\n\nAnd on the other hand what means the phrase 'very complex'? I have\nalready given one solution, but there are others. Complex causes we have\nsaid produce a blend more and more intimate, but after how long a time\nwill this blend satisfy us? When will it have accumulated sufficient\ncomplexity? When shall we have sufficiently shuffled the cards? If we\nmix two powders, one blue, the other white, there comes a moment when\nthe tint of the mixture seems to us uniform because of the feebleness of\nour senses; it will be uniform for the presbyte, forced to gaze from\nafar, before it will be so for the myope. And when it has become uniform\nfor all eyes, we still could push back the limit by the use of\ninstruments. There is no chance for any man ever to discern the infinite\nvariety which, if the kinetic theory is true, hides under the uniform\nappearance of a gas. And yet if we accept Gouy's ideas on the Brownian\nmovement, does not the microscope seem on the point of showing us\nsomething analogous?\n\nThis new criterion is therefore relative like the first; and if it\nretains an objective character, it is because all men have approximately\nthe same senses, the power of their instruments is limited, and besides\nthey use them only exceptionally.\n\n\nIX\n\nIt is just the same in the moral sciences and particularly in history.\nThe historian is obliged to make a choice among the events of the epoch\nhe studies; he recounts only those which seem to him the most important.\nHe therefore contents himself with relating the most momentous events of\nthe sixteenth century, for example, as likewise the most remarkable\nfacts of the seventeenth century. If the first suffice to explain the\nsecond, we say these conform to the laws of history. But if a great\nevent of the seventeenth century should have for cause a small fact of\nthe sixteenth century which no history reports, which all the world has\nneglected, then we say this event is due to chance. This word has\ntherefore the same sense as in the physical sciences; it means that\nslight causes have produced great effects.\n\nThe greatest bit of chance is the birth of a great man. It is only by\nchance that meeting of two germinal cells, of different sex, containing\nprecisely, each on its side, the mysterious elements whose mutual\nreaction must produce the genius. One will agree that these elements\nmust be rare and that their meeting is still more rare. How slight a\nthing it would have required to deflect from its route the carrying\nspermatozoon. It would have sufficed to deflect it a tenth of a\nmillimeter and Napoleon would not have been born and the destinies of a\ncontinent would have been changed. No example can better make us\nunderstand the veritable characteristics of chance.\n\nOne more word about the paradoxes brought out by the application of the\ncalculus of probabilities to the moral sciences. It has been proven that\nno Chamber of Deputies will ever fail to contain a member of the\nopposition, or at least such an event would be so improbable that we\nmight without fear wager the contrary, and bet a million against a sou.\n\nCondorcet has striven to calculate how many jurors it would require to\nmake a judicial error practically impossible. If we had used the results\nof this calculation, we should certainly have been exposed to the same\ndisappointments as in betting, on the faith of the calculus, that the\nopposition would never be without a representative.\n\nThe laws of chance do not apply to these questions. If justice be not\nalways meted out to accord with the best reasons, it uses less than we\nthink the method of Bridoye. This is perhaps to be regretted, for then\nthe system of Condorcet would shield us from judicial errors.\n\nWhat is the meaning of this? We are tempted to attribute facts of this\nnature to chance because their causes are obscure; but this is not true\nchance. The causes are unknown to us, it is true, and they are even\ncomplex; but they are not sufficiently so, since they conserve\nsomething. We have seen that this it is which distinguishes causes 'too\nsimple.' When men are brought together they no longer decide at random\nand independently one of another; they influence one another. Multiplex\ncauses come into action. They worry men, dragging them to right or left,\nbut one thing there is they can not destroy, this is their Panurge\nflock-of-sheep habits. And this is an invariant.\n\n\nX\n\nDifficulties are indeed involved in the application of the calculus of\nprobabilities to the exact sciences. Why are the decimals of a table of\nlogarithms, why are those of the number [pi] distributed in accordance\nwith the laws of chance? Elsewhere I have already studied the question\nin so far as it concerns logarithms, and there it is easy. It is clear\nthat a slight difference of argument will give a slight difference of\nlogarithm, but a great difference in the sixth decimal of the logarithm.\nAlways we find again the same criterion.\n\nBut as for the number [pi], that presents more difficulties, and I have\nat the moment nothing worth while to say.\n\nThere would be many other questions to resolve, had I wished to attack\nthem before solving that which I more specially set myself. When we\nreach a simple result, when we find for example a round number, we say\nthat such a result can not be due to chance, and we seek, for its\nexplanation, a non-fortuitous cause. And in fact there is only a very\nslight probability that among 10,000 numbers chance will give a round\nnumber; for example, the number 10,000. This has only one chance in\n10,000. But there is only one chance in 10,000 for the occurrence of any\nother one number; and yet this result will not astonish us, nor will it\nbe hard for us to attribute it to chance; and that simply because it\nwill be less striking.\n\nIs this a simple illusion of ours, or are there cases where this way of\nthinking is legitimate? We must hope so, else were all science\nimpossible. When we wish to check a hypothesis, what do we do? We can\nnot verify all its consequences, since they would be infinite in number;\nwe content ourselves with verifying certain ones and if we succeed we\ndeclare the hypothesis confirmed, because so much success could not be\ndue to chance. And this is always at bottom the same reasoning.\n\nI can not completely justify it here, since it would take too much time;\nbut I may at least say that we find ourselves confronted by two\nhypotheses, either a simple cause or that aggregate of complex causes we\ncall chance. We find it natural to suppose that the first should produce\na simple result, and then, if we find that simple result, the round\nnumber for example, it seems more likely to us to be attributable to the\nsimple cause which must give it almost certainly, than to chance which\ncould only give it once in 10,000 times. It will not be the same if we\nfind a result which is not simple; chance, it is true, will not give\nthis more than once in 10,000 times; but neither has the simple cause\nany more chance of producing it.\n\n\n\n\nBOOK II\n\n\nMATHEMATICAL REASONING\n\n\n\n\nCHAPTER I\n\nTHE RELATIVITY OF SPACE\n\n\nI\n\nIt is impossible to represent to oneself empty space; all our efforts to\nimagine a pure space, whence should be excluded the changing images of\nmaterial objects, can result only in a representation where vividly\ncolored surfaces, for example, are replaced by lines of faint\ncoloration, and we can not go to the very end in this way without all\nvanishing and terminating in nothingness. Thence comes the irreducible\nrelativity of space.\n\nWhoever speaks of absolute space uses a meaningless phrase. This is a\ntruth long proclaimed by all who have reflected upon the matter, but\nwhich we are too often led to forget.\n\nI am at a determinate point in Paris, place du Panth\u00e9on for instance,\nand I say: I shall come back _here_ to-morrow. If I be asked: Do you\nmean you will return to the same point of space, I shall be tempted to\nanswer: yes; and yet I shall be wrong, since by to-morrow the earth will\nhave journeyed hence, carrying with it the place du Panth\u00e9on, which will\nhave traveled over more than two million kilometers. And if I tried to\nspeak more precisely, I should gain nothing, since our globe has run\nover these two million kilometers in its motion with relation to the\nsun, while the sun in its turn is displaced with reference to the Milky\nWay, while the Milky Way itself is doubtless in motion without our being\nable to perceive its velocity. So that we are completely ignorant, and\nalways shall be, of how much the place du Panth\u00e9on is displaced in a\nday.\n\nIn sum, I meant to say: To-morrow I shall see again the dome and the\npediment of the Panth\u00e9on, and if there were no Panth\u00e9on my phrase would\nbe meaningless and space would vanish.\n\nThis is one of the most commonplace forms of the principle of the\nrelativity of space; but there is another, upon which Delbeuf has\nparticularly insisted. Suppose that in the night all the dimensions of\nthe universe become a thousand times greater: the world will have\nremained _similar_ to itself, giving to the word _similitude_ the same\nmeaning as in Euclid, Book VI. Only what was a meter long will measure\nthenceforth a kilometer, what was a millimeter long will become a meter.\nThe bed whereon I lie and my body itself will be enlarged in the same\nproportion.\n\nWhen I awake to-morrow morning, what sensation shall I feel in presence\nof such an astounding transformation? Well, I shall perceive nothing at\nall. The most precise measurements will be incapable of revealing to me\nanything of this immense convulsion, since the measures I use will have\nvaried precisely in the same proportion as the objects I seek to\nmeasure. In reality, this convulsion exists only for those who reason as\nif space were absolute. If I for a moment have reasoned as they do, it\nis the better to bring out that their way of seeing implies\ncontradiction. In fact it would be better to say that, space being\nrelative, nothing at all has happened, which is why we have perceived\nnothing.\n\nHas one the right, therefore, to say he knows the distance between two\npoints? No, since this distance could undergo enormous variations\nwithout our being able to perceive them, provided the other distances\nhave varied in the same proportion. We have just seen that when I say: I\nshall be here to-morrow, this does not mean: To-morrow I shall be at the\nsame point of space where I am to-day, but rather: To-morrow I shall be\nat the same distance from the Panth\u00e9on as to-day. And we see that this\nstatement is no longer sufficient and that I should say: To-morrow and\nto-day my distance from the Panth\u00e9on will be equal to the same number of\ntimes the height of my body.\n\nBut this is not all; I have supposed the dimensions of the world to\nvary, but that at least the world remained always similar to itself. We\nmight go much further, and one of the most astonishing theories of\nmodern physics furnishes us the occasion.\n\nAccording to Lorentz and Fitzgerald, all the bodies borne along in the\nmotion of the earth undergo a deformation.\n\nThis deformation is, in reality, very slight, since all dimensions\nparallel to the movement of the earth diminish by a hundred millionth,\nwhile the dimensions perpendicular to this movement are unchanged. But\nit matters little that it is slight, that it exists suffices for the\nconclusion I am about to draw. And besides, I have said it was slight,\nbut in reality I know nothing about it; I have myself been victim of the\ntenacious illusion which makes us believe we conceive an absolute space;\nI have thought of the motion of the earth in its elliptic orbit around\nthe sun, and I have allowed thirty kilometers as its velocity. But its\nreal velocity (I mean, this time, not its absolute velocity, which is\nmeaningless, but its velocity with relation to the ether), I do not know\nthat, and have no means of knowing it: it is perhaps, 10, 100 times\ngreater, and then the deformation will be 100, 10,000 times more.\n\nCan we show this deformation? Evidently not; here is a cube with edge\none meter; in consequence of the earth's displacement it is deformed,\none of its edges, that parallel to the motion, becomes smaller, the\nothers do not change. If I wish to assure myself of it by aid of a meter\nmeasure, I shall measure first one of the edges perpendicular to the\nmotion and shall find that my standard meter fits this edge exactly; and\nin fact neither of these two lengths is changed, since both are\nperpendicular to the motion. Then I wish to measure the other edge, that\nparallel to the motion; to do this I displace my meter and turn it so as\nto apply it to the edge. But the meter, having changed orientation and\nbecome parallel to the motion, has undergone, in its turn, the\ndeformation, so that though the edge be not a meter long, it will fit\nexactly, I shall find out nothing.\n\nYou ask then of what use is the hypothesis of Lorentz and of Fitzgerald\nif no experiment can permit of its verification? It is my exposition\nthat has been incomplete; I have spoken only of measurements that can be\nmade with a meter; but we can also measure a length by the time it takes\nlight to traverse it, on condition we suppose the velocity of light\nconstant and independent of direction. Lorentz could have accounted for\nthe facts by supposing the velocity of light greater in the direction\nof the earth's motion than in the perpendicular direction. He preferred\nto suppose that the velocity is the same in these different directions\nbut that the bodies are smaller in the one than in the other. If the\nwave surfaces of light had undergone the same deformations as the\nmaterial bodies we should never have perceived the Lorentz-Fitzgerald\ndeformation.\n\nIn either case, it is not a question of absolute magnitude, but of the\nmeasure of this magnitude by means of some instrument; this instrument\nmay be a meter, or the path traversed by light; it is only the relation\nof the magnitude to the instrument that we measure; and if this relation\nis altered, we have no way of knowing whether it is the magnitude or the\ninstrument which has changed.\n\nBut what I wish to bring out is, that in this deformation the world has\nnot remained similar to itself; squares have become rectangles, circles\nellipses, spheres ellipsoids. And yet we have no way of knowing whether\nthis deformation be real.\n\nEvidently one could go much further: in place of the Lorentz-Fitzgerald\ndeformation, whose laws are particularly simple, we could imagine any\ndeformation whatsoever. Bodies could be deformed according to any laws,\nas complicated as we might wish, we never should notice it provided all\nbodies without exception were deformed according to the same laws. In\nsaying, all bodies without exception, I include of course our own body\nand the light rays emanating from different objects.\n\nIf we look at the world in one of those mirrors of complicated shape\nwhich deform objects in a bizarre way, the mutual relations of the\ndifferent parts of this world would not be altered; if, in fact two real\nobjects touch, their images likewise seem to touch. Of course when we\nlook in such a mirror we see indeed the deformation, but this is because\nthe real world subsists alongside of its deformed image; and then even\nwere this real world hidden from us, something there is could not be\nhidden, ourself; we could not cease to see, or at least to feel, our\nbody and our limbs which have not been deformed and which continue to\nserve us as instruments of measure.\n\nBut if we imagine our body itself deformed in the same way as if seen\nin the mirror, these instruments of measure in their turn will fail us\nand the deformation will no longer be ascertainable.\n\nConsider in the same way two worlds images of one another; to each\nobject _P_ of the world _A_ corresponds in the world _B_ an object _P'_,\nits image; the coordinates of this image _P'_ are determinate functions\nof those of the object _P_; moreover these functions may be any\nwhatsoever; I only suppose them chosen once for all. Between the\nposition of _P_ and that of _P'_ there is a constant relation; what this\nrelation is, matters not; enough that it be constant.\n\nWell, these two worlds will be indistinguishable one from the other. I\nmean the first will be for its inhabitants what the second is for its.\nAnd so it will be as long as the two worlds remain strangers to each\nother. Suppose we lived in world _A_, we shall have constructed our\nscience and in particular our geometry; during this time the inhabitants\nof world _B_ will have constructed a science, and as their world is the\nimage of ours, their geometry will also be the image of ours or, better,\nit will be the same. But if for us some day a window is opened upon\nworld _B_, how we shall pity them: \"Poor things,\" we shall say, \"they\nthink they have made a geometry, but what they call so is only a\ngrotesque image of ours; their straights are all twisted, their circles\nare humped, their spheres have capricious inequalities.\" And we shall\nnever suspect they say the same of us, and one never will know who is\nright.\n\nWe see in how broad a sense should be understood the relativity of\nspace; space is in reality amorphous and the things which are therein\nalone give it a form. What then should be thought of that direct\nintuition we should have of the straight or of distance? So little have\nwe intuition of distance in itself that in the night, as we have said, a\ndistance might become a thousand times greater without our being able to\nperceive it, if all other distances had undergone the same alteration.\nAnd even in a night the world _B_ might be substituted for the world _A_\nwithout our having any way of knowing it, and then the straight lines of\nyesterday would have ceased to be straight and we should never notice.\n\nOne part of space is not by itself and in the absolute sense of the word\nequal to another part of space; because if so it is for us, it would not\nbe for the dwellers in world _B_; and these have just as much right to\nreject our opinion as we to condemn theirs.\n\nI have elsewhere shown what are the consequences of these facts from the\nviewpoint of the idea we should form of non-Euclidean geometry and other\nanalogous geometries; to that I do not care to return; and to-day I\nshall take a somewhat different point of view.\n\n\nII\n\nIf this intuition of distance, of direction, of the straight line, if\nthis direct intuition of space in a word does not exist, whence comes\nour belief that we have it? If this is only an illusion, why is this\nillusion so tenacious? It is proper to examine into this. We have said\nthere is no direct intuition of size and we can only arrive at the\nrelation of this magnitude to our instruments of measure. We should\ntherefore not have been able to construct space if we had not had an\ninstrument to measure it; well, this instrument to which we relate\neverything, which we use instinctively, it is our own body. It is in\nrelation to our body that we place exterior objects, and the only\nspatial relations of these objects that we can represent are their\nrelations to our body. It is our body which serves us, so to speak, as\nsystem of axes of coordinates.\n\nFor example, at an instant [alpha], the presence of the object _A_ is\nrevealed to me by the sense of sight; at another instant, [beta], the\npresence of another object, _B_, is revealed to me by another sense,\nthat of hearing or of touch, for instance. I judge that this object _B_\noccupies the same place as the object _A_. What does that mean? First\nthat does not signify that these two objects occupy, at two different\nmoments, the same point of an absolute space, which even if it existed\nwould escape our cognition, since, between the instants [alpha] and\n[beta], the solar system has moved and we can not know its displacement.\nThat means these two objects occupy the same relative position with\nreference to our body.\n\nBut even this, what does it mean? The impressions that have come to us\nfrom these objects have followed paths absolutely different, the optic\nnerve for the object _A_, the acoustic nerve for the object _B_.\nThey have nothing in common from the qualitative point of view. The\nrepresentations we are able to make of these two objects are absolutely\nheterogeneous, irreducible one to the other. Only I know that to reach\nthe object _A_ I have just to extend the right arm in a certain way;\neven when I abstain from doing it, I represent to myself the muscular\nsensations and other analogous sensations which would accompany this\nextension, and this representation is associated with that of the\nobject _A_.\n\nNow, I likewise know I can reach the object _B_ by extending my right\narm in the same manner, an extension accompanied by the same train of\nmuscular sensations. And when I say these two objects occupy the same\nplace, I mean nothing more.\n\nI also know I could have reached the object _A_ by another appropriate\nmotion of the left arm and I represent to myself the muscular sensations\nwhich would have accompanied this movement; and by this same motion of\nthe left arm, accompanied by the same sensations, I likewise could have\nreached the object _B_.\n\nAnd that is very important, since thus I can defend myself against\ndangers menacing me from the object _A_ or the object _B_. With each of\nthe blows we can be hit, nature has associated one or more parries which\npermit of our guarding ourselves. The same parry may respond to several\nstrokes; and so it is, for instance, that the same motion of the right\narm would have allowed us to guard at the instant [alpha] against the\nobject _A_ and at the instant [beta] against the object _B_. Just so,\nthe same stroke can be parried in several ways, and we have said, for\ninstance, the object _A_ could be reached indifferently either by a\ncertain movement of the right arm or by a certain movement of the left\narm.\n\nAll these parries have nothing in common except warding off the same\nblow, and this it is, and nothing else, which is meant when we say they\nare movements terminating at the same point of space. Just so, these\nobjects, of which we say they occupy the same point of space, have\nnothing in common, except that the same parry guards against them.\n\nOr, if you choose, imagine innumerable telegraph wires, some\ncentripetal, others centrifugal. The centripetal wires warn us of\naccidents happening without; the centrifugal wires carry the reparation.\nConnections are so established that when a centripetal wire is traversed\nby a current this acts on a relay and so starts a current in one of the\ncentrifugal wires, and things are so arranged that several centripetal\nwires may act on the same centrifugal wire if the same remedy suits\nseveral ills, and that a centripetal wire may agitate different\ncentrifugal wires, either simultaneously or in lieu one of the other\nwhen the same ill may be cured by several remedies.\n\nIt is this complex system of associations, it is this table of\ndistribution, so to speak, which is all our geometry or, if you wish,\nall in our geometry that is instinctive. What we call our intuition of\nthe straight line or of distance is the consciousness we have of these\nassociations and of their imperious character.\n\nAnd it is easy to understand whence comes this imperious character\nitself. An association will seem to us by so much the more\nindestructible as it is more ancient. But these associations are not,\nfor the most part, conquests of the individual, since their trace is\nseen in the new-born babe: they are conquests of the race. Natural\nselection had to bring about these conquests by so much the more quickly\nas they were the more necessary.\n\nOn this account, those of which we speak must have been of the earliest\nin date, since without them the defense of the organism would have been\nimpossible. From the time when the cellules were no longer merely\njuxtaposed, but were called upon to give mutual aid, it was needful that\na mechanism organize analogous to what we have described, so that this\naid miss not its way, but forestall the peril.\n\nWhen a frog is decapitated, and a drop of acid is placed on a point of\nits skin, it seeks to wipe off the acid with the nearest foot, and, if\nthis foot be amputated, it sweeps it off with the foot of the opposite\nside. There we have the double parry of which I have just spoken,\nallowing the combating of an ill by a second remedy, if the first fails.\nAnd it is this multiplicity of parries, and the resulting coordination,\nwhich is space.\n\nWe see to what depths of the unconscious we must descend to find the\nfirst traces of these spatial associations, since only the inferior\nparts of the nervous system are involved. Why be astonished then at the\nresistance we oppose to every attempt made to dissociate what so long\nhas been associated? Now, it is just this resistance that we call the\nevidence for the geometric truths; this evidence is nothing but the\nrepugnance we feel toward breaking with very old habits which have\nalways proved good.\n\n\nIII\n\nThe space so created is only a little space extending no farther than my\narm can reach; the intervention of the memory is necessary to push back\nits limits. There are points which will remain out of my reach, whatever\neffort I make to stretch forth my hand; if I were fastened to the ground\nlike a hydra polyp, for instance, which can only extend its tentacles,\nall these points would be outside of space, since the sensations we\ncould experience from the action of bodies there situated, would be\nassociated with the idea of no movement allowing us to reach them, of no\nappropriate parry. These sensations would not seem to us to have any\nspatial character and we should not seek to localize them.\n\nBut we are not fixed to the ground like the lower animals; we can, if\nthe enemy be too far away, advance toward him first and extend the hand\nwhen we are sufficiently near. This is still a parry, but a parry at\nlong range. On the other hand, it is a complex parry, and into the\nrepresentation we make of it enter the representation of the muscular\nsensations caused by the movements of the legs, that of the muscular\nsensations caused by the final movement of the arm, that of the\nsensations of the semicircular canals, etc. We must, besides, represent\nto ourselves, not a complex of simultaneous sensations, but a complex of\nsuccessive sensations, following each other in a determinate order, and\nthis is why I have just said the intervention of memory was necessary.\nNotice moreover that, to reach the same point, I may approach nearer the\nmark to be attained, so as to have to stretch my arm less. What more? It\nis not one, it is a thousand parries I can oppose to the same danger.\nAll these parries are made of sensations which may have nothing in\ncommon and yet we regard them as defining the same point of space, since\nthey may respond to the same danger and are all associated with the\nnotion of this danger. It is the potentiality of warding off the same\nstroke which makes the unity of these different parries, as it is the\npossibility of being parried in the same way which makes the unity of\nthe strokes so different in kind, which may menace us from the same\npoint of space. It is this double unity which makes the individuality of\neach point of space, and, in the notion of point, there is nothing else.\n\nThe space before considered, which might be called _restricted space_,\nwas referred to coordinate axes bound to my body; these axes were fixed,\nsince my body did not move and only my members were displaced. What are\nthe axes to which we naturally refer the _extended space_? that is to\nsay the new space just defined. We define a point by the sequence of\nmovements to be made to reach it, starting from a certain initial\nposition of the body. The axes are therefore fixed to this initial\nposition of the body.\n\nBut the position I call initial may be arbitrarily chosen among all the\npositions my body has successively occupied; if the memory more or less\nunconscious of these successive positions is necessary for the genesis\nof the notion of space, this memory may go back more or less far into\nthe past. Thence results in the definition itself of space a certain\nindetermination, and it is precisely this indetermination which\nconstitutes its relativity.\n\nThere is no absolute space, there is only space relative to a certain\ninitial position of the body. For a conscious being fixed to the ground\nlike the lower animals, and consequently knowing only restricted space,\nspace would still be relative (since it would have reference to his\nbody), but this being would not be conscious of this relativity, because\nthe axes of reference for this restricted space would be unchanging!\nDoubtless the rock to which this being would be fettered would not be\nmotionless, since it would be carried along in the movement of our\nplanet; for us consequently these axes would change at each instant; but\nfor him they would be changeless. We have the faculty of referring our\nextended space now to the position _A_ of our body, considered as\ninitial, again to the position _B_, which it had some moments afterward,\nand which we are free to regard in its turn as initial; we make\ntherefore at each instant unconscious transformations of coordinates.\nThis faculty would be lacking in our imaginary being, and from not\nhaving traveled, he would think space absolute. At every instant, his\nsystem of axes would be imposed upon him; this system would have to\nchange greatly in reality, but for him it would be always the same,\nsince it would be always the _only_ system. Quite otherwise is it with\nus, who at each instant have many systems between which we may choose at\nwill, on condition of going back by memory more or less far into the\npast.\n\nThis is not all; restricted space would not be homogeneous; the\ndifferent points of this space could not be regarded as equivalent,\nsince some could be reached only at the cost of the greatest efforts,\nwhile others could be easily attained. On the contrary, our extended\nspace seems to us homogeneous, and we say all its points are equivalent.\nWhat does that mean?\n\nIf we start from a certain place _A_, we can, from this position, make\ncertain movements, _M_, characterized by a certain complex of muscular\nsensations. But, starting from another position, _B_, we make movements\n_M'_ characterized by the same muscular sensations. Let _a_, then, be\nthe situation of a certain point of the body, the end of the index\nfinger of the right hand for example, in the initial position _A_, and\n_b_ the situation of this same index when, starting from this position\n_A_, we have made the motions _M_. Afterwards, let _a'_ be the situation\nof this index in the position _B_, and _b'_ its situation when, starting\nfrom the position _B_, we have made the motions _M'_.\n\nWell, I am accustomed to say that the points of space _a_ and _b_ are\nrelated to each other just as the points _a'_ and _b'_, and this simply\nmeans that the two series of movements _M_ and _M'_ are accompanied by\nthe same muscular sensations. And as I am conscious that, in passing\nfrom the position _A_ to the position _B_, my body has remained capable\nof the same movements, I know there is a point of space related to the\npoint _a'_ just as any point _b_ is to the point _a_, so that the two\npoints _a_ and _a'_ are equivalent. This is what is called the\nhomogeneity of space. And, at the same time, this is why space is\nrelative, since its properties remain the same whether it be referred to\nthe axes _A_ or to the axes _B_. So that the relativity of space and its\nhomogeneity are one sole and same thing.\n\nNow, if I wish to pass to the great space, which no longer serves only\nfor me, but where I may lodge the universe, I get there by an act of\nimagination. I imagine how a giant would feel who could reach the\nplanets in a few steps; or, if you choose, what I myself should feel in\npresence of a miniature world where these planets were replaced by\nlittle balls, while on one of these little balls moved a liliputian I\nshould call myself. But this act of imagination would be impossible for\nme had I not previously constructed my restricted space and my extended\nspace for my own use.\n\n\nIV\n\nWhy now have all these spaces three dimensions? Go back to the \"table of\ndistribution\" of which we have spoken. We have on the one side the list\nof the different possible dangers; designate them by _A1_, _A2_, etc.;\nand, on the other side, the list of the different remedies which I shall\ncall in the same way _B1_, _B2_, etc. We have then connections between\nthe contact studs or push buttons of the first list and those of the\nsecond, so that when, for instance, the announcer of danger _A3_\nfunctions, it will put or may put in action the relay corresponding to\nthe parry _B4_.\n\nAs I have spoken above of centripetal or centrifugal wires, I fear lest\none see in all this, not a simple comparison, but a description of the\nnervous system. Such is not my thought, and that for several reasons:\nfirst I should not permit myself to put forth an opinion on the\nstructure of the nervous system which I do not know, while those who\nhave studied it speak only circumspectly; again because, despite my\nincompetence, I well know this scheme would be too simplistic; and\nfinally because on my list of parries, some would figure very complex,\nwhich might even, in the case of extended space, as we have seen above,\nconsist of many steps followed by a movement of the arm. It is not a\nquestion then of physical connection between two real conductors but of\npsychologic association between two series of sensations.\n\nIf _A1_ and _A2_ for instance are both associated with the parry _B1_,\nand if _A1_ is likewise associated with the parry _B2_, it will\ngenerally happen that _A2_ and _B2_ will also themselves be associated.\nIf this fundamental law were not generally true, there would exist only\nan immense confusion and there would be nothing resembling a conception\nof space or a geometry. How in fact have we defined a point of space. We\nhave done it in two ways: it is on the one hand the aggregate of\nannouncers _A_ in connection with the same parry _B_; it is on the other\nhand the aggregate of parries _B_ in connection with the same announcer\n_A_. If our law was not true, we should say _A1_ and _A2_ correspond to\nthe same point since they are both in connection with _B1_; but we\nshould likewise say they do not correspond to the same point, since _A1_\nwould be in connection with _B2_ and the same would not be true of _A2_.\nThis would be a contradiction.\n\nBut, from another side, if the law were rigorously and always true,\nspace would be very different from what it is. We should have categories\nstrongly contrasted between which would be portioned out on the one hand\nthe announcers _A_, on the other hand the parries _B_; these categories\nwould be excessively numerous, but they would be entirely separated one\nfrom another. Space would be composed of points very numerous, but\ndiscrete; it would be _discontinuous_. There would be no reason for\nranging these points in one order rather than another, nor consequently\nfor attributing to space three dimensions.\n\nBut it is not so; permit me to resume for a moment the language of those\nwho already know geometry; this is quite proper since this is the\nlanguage best understood by those I wish to make understand me.\n\nWhen I desire to parry the stroke, I seek to attain the point whence\ncomes this blow, but it suffices that I approach quite near. Then the\nparry _B1_ may answer for _A1_ and for _A2_, if the point which\ncorresponds to _B1_ is sufficiently near both to that corresponding to\n_A1_ and to that corresponding to _A2_. But it may happen that the point\ncorresponding to another parry _B2_ may be sufficiently near to the\npoint corresponding to A1 and not sufficiently near the point\ncorresponding to _A2_; so that the parry _B2_ may answer for _A1_\nwithout answering for _A2_. For one who does not yet know geometry, this\ntranslates itself simply by a derogation of the law stated above. And\nthen things will happen thus:\n\nTwo parries _B1_ and _B2_ will be associated with the same warning _A1_\nand with a large number of warnings which we shall range in the same\ncategory as _A1_ and which we shall make correspond to the same point of\nspace. But we may find warnings _A2_ which will be associated with _B2_\nwithout being associated with _B1_, and which in compensation will be\nassociated with _B3_, which _B3_ was not associated with _A1_, and so\nforth, so that we may write the series\n\n _B1_, _A1_, _B2_, _A2_, _B3_, _A3_, _B4_, _A4_,\n\nwhere each term is associated with the following and the preceding, but\nnot with the terms several places away.\n\nNeedless to add that each of the terms of these series is not isolated,\nbut forms part of a very numerous category of other warnings or of other\nparries which have the same connections as it, and which may be regarded\nas belonging to the same point of space.\n\nThe fundamental law, though admitting of exceptions, remains therefore\nalmost always true. Only, in consequence of these exceptions, these\ncategories, in place of being entirely separated, encroach partially one\nupon another and mutually penetrate in a certain measure, so that space\nbecomes continuous.\n\nOn the other hand, the order in which these categories are to be ranged\nis no longer arbitrary, and if we refer to the preceding series, we see\nit is necessary to put _B2_ between _A1_ and _A2_ and consequently\nbetween _B1_ and _B3_ and that we could not for instance put it between\n_B3_ and _B4_.\n\nThere is therefore an order in which are naturally arranged our\ncategories which correspond to the points of space, and experience\nteaches us that this order presents itself under the form of a table\nof triple entry, and this is why space has three dimensions.\n\n\nV\n\nSo the characteristic property of space, that of having three\ndimensions, is only a property of our table of distribution, an internal\nproperty of the human intelligence, so to speak. It would suffice to\ndestroy certain of these connections, that is to say of the associations\nof ideas to give a different table of distribution, and that might be\nenough for space to acquire a fourth dimension.\n\nSome persons will be astonished at such a result. The external world,\nthey will think, should count for something. If the number of dimensions\ncomes from the way we are made, there might be thinking beings living in\nour world, but who might be made differently from us and who would\nbelieve space has more or less than three dimensions. Has not M. de Cyon\nsaid that the Japanese mice, having only two pair of semicircular\ncanals, believe that space is two-dimensional? And then this thinking\nbeing, if he is capable of constructing a physics, would he not make a\nphysics of two or of four dimensions, and which in a sense would still\nbe the same as ours, since it would be the description of the same world\nin another language?\n\nIt seems in fact that it would be possible to translate our physics into\nthe language of geometry of four dimensions; to attempt this translation\nwould be to take great pains for little profit, and I shall confine\nmyself to citing the mechanics of Hertz where we have something\nanalogous. However, it seems that the translation would always be less\nsimple than the text, and that it would always have the air of a\ntranslation, that the language of three dimensions seems the better\nfitted to the description of our world, although this description can be\nrigorously made in another idiom. Besides, our table of distribution was\nnot made at random. There is connection between the warning _A1_ and the\nparry _B1_, this is an internal property of our intelligence; but why\nthis connection? It is because the parry _B1_ affords means effectively\nto guard against the danger _A1_; and this is a fact exterior to us,\nthis is a property of the exterior world. Our table of distribution is\ntherefore only the translation of an aggregate of exterior facts; if it\nhas three dimensions, this is because it has adapted itself to a world\nhaving certain properties; and the chief of these properties is that\nthere exist natural solids whose displacements follow sensibly the laws\nwe call laws of motion of rigid solids. If therefore the language of\nthree dimensions is that which permits us most easily to describe our\nworld, we should not be astonished; this language is copied from our\ntable of distribution; and it is in order to be able to live in this\nworld that this table has been established.\n\nI have said we could conceive, living in our world, thinking beings\nwhose table of distribution would be four-dimensional and who\nconsequently would think in hyperspace. It is not certain however that\nsuch beings, admitting they were born there, could live there and defend\nthemselves against the thousand dangers by which they would there be\nassailed.\n\n\nVI\n\nA few remarks to end with. There is a striking contrast between the\nroughness of this primitive geometry, reducible to what I call a table\nof distribution, and the infinite precision of the geometers' geometry.\nAnd yet this is born of that; but not of that alone; it must be made\nfecund by the faculty we have of constructing mathematical concepts,\nsuch as that of group, for instance; it was needful to seek among the\npure concepts that which best adapts itself to this rough space whose\ngenesis I have sought to explain and which is common to us and the\nhigher animals.\n\nThe evidence for certain geometric postulates, we have said, is only our\nrepugnance to renouncing very old habits. But these postulates are\ninfinitely precise, while these habits have something about them\nessentially pliant. When we wish to think, we need postulates infinitely\nprecise, since this is the only way to avoid contradiction; but among\nall the possible systems of postulates, there are some we dislike to\nchoose because they are not sufficiently in accord with our habits;\nhowever pliant, however elastic they may be, these have a limit of\nelasticity.\n\nWe see that if geometry is not an experimental science, it is a science\nborn apropos of experience; that we have created the space it studies,\nbut adapting it to the world wherein we live. We have selected the most\nconvenient space, but experience has guided our choice; as this choice\nhas been unconscious, we think it has been imposed upon us; some say\nexperience imposes it, others that we are born with our space ready\nmade; we see from the preceding considerations, what in these two\nopinions is the part of truth, what of error.\n\nIn this progressive education whose outcome has been the construction of\nspace, it is very difficult to determine what is the part of the\nindividual, what the part of the race. How far could one of us,\ntransported from birth to an entirely different world, where were\ndominant, for instance, bodies moving in conformity to the laws of\nmotion of non-Euclidean solids, renounce the ancestral space to build a\nspace completely new?\n\nThe part of the race seems indeed preponderant; yet if to it we owe\nrough space, the soft space I have spoken of, the space of the higher\nanimals, is it not to the unconscious experience of the individual we\nowe the infinitely precise space of the geometer? This is a question not\neasy to solve. Yet we cite a fact showing that the space our ancestors\nhave bequeathed us still retains a certain plasticity. Some hunters\nlearn to shoot fish under water, though the image of these fish be\nturned up by refraction. Besides they do it instinctively: they\ntherefore have learned to modify their old instinct of direction; or, if\nyou choose, to substitute for the association _A1_, _B1_, another\nassociation _A1_, _B2_, because experience showed them the first would\nnot work.\n\n\n\n\nCHAPTER II\n\nMATHEMATICAL DEFINITIONS AND TEACHING\n\n\n1. I should speak here of general definitions in mathematics; at least\nthat is the title, but it will be impossible to confine myself to the\nsubject as strictly as the rule of unity of action would require; I\nshall not be able to treat it without touching upon a few other related\nquestions, and if thus I am forced from time to time to walk on the\nbordering flower-beds on the right or left, I pray you bear with me.\n\nWhat is a good definition? For the philosopher or the scientist it is a\ndefinition which applies to all the objects defined, and only those; it\nis the one satisfying the rules of logic. But in teaching it is not\nthat; a good definition is one understood by the scholars.\n\nHow does it happen that so many refuse to understand mathematics? Is\nthat not something of a paradox? Lo and behold! a science appealing only\nto the fundamental principles of logic, to the principle of\ncontradiction, for instance, to that which is the skeleton, so to speak,\nof our intelligence, to that of which we can not divest ourselves\nwithout ceasing to think, and there are people who find it obscure! and\nthey are even in the majority! That they are incapable of inventing may\npass, but that they do not understand the demonstrations shown them,\nthat they remain blind when we show them a light which seems to us\nflashing pure flame, this it is which is altogether prodigious.\n\nAnd yet there is no need of a wide experience with examinations to know\nthat these blind men are in no wise exceptional beings. This is a\nproblem not easy to solve, but which should engage the attention of all\nthose wishing to devote themselves to teaching.\n\nWhat is it, to understand? Has this word the same meaning for all the\nworld? To understand the demonstration of a theorem, is that to examine\nsuccessively each of the syllogisms composing it and to ascertain its\ncorrectness, its conformity to the rules of the game? Likewise, to\nunderstand a definition, is this merely to recognize that one already\nknows the meaning of all the terms employed and to ascertain that it\nimplies no contradiction?\n\nFor some, yes; when they have done this, they will say: I understand.\n\nFor the majority, no. Almost all are much more exacting; they wish to\nknow not merely whether all the syllogisms of a demonstration are\ncorrect, but why they link together in this order rather than another.\nIn so far as to them they seem engendered by caprice and not by an\nintelligence always conscious of the end to be attained, they do not\nbelieve they understand.\n\nDoubtless they are not themselves just conscious of what they crave and\nthey could not formulate their desire, but if they do not get\nsatisfaction, they vaguely feel that something is lacking. Then what\nhappens? In the beginning they still perceive the proofs one puts under\ntheir eyes; but as these are connected only by too slender a thread to\nthose which precede and those which follow, they pass without leaving\nany trace in their head; they are soon forgotten; a moment bright, they\nquickly vanish in night eternal. When they are farther on, they will no\nlonger see even this ephemeral light, since the theorems lean one upon\nanother and those they would need are forgotten; thus it is they become\nincapable of understanding mathematics.\n\nThis is not always the fault of their teacher; often their mind, which\nneeds to perceive the guiding thread, is too lazy to seek and find it.\nBut to come to their aid, we first must know just what hinders them.\n\nOthers will always ask of what use is it; they will not have understood\nif they do not find about them, in practise or in nature, the\njustification of such and such a mathematical concept. Under each word\nthey wish to put a sensible image; the definition must evoke this image,\nso that at each stage of the demonstration they may see it transform and\nevolve. Only upon this condition do they comprehend and retain. Often\nthese deceive themselves; they do not listen to the reasoning, they look\nat the figures; they think they have understood and they have only seen.\n\n2. How many different tendencies! Must we combat them? Must we use them?\nAnd if we wish to combat them, which should be favored? Must we show\nthose content with the pure logic that they have seen only one side of\nthe matter? Or need we say to those not so cheaply satisfied that what\nthey demand is not necessary?\n\nIn other words, should we constrain the young people to change the\nnature of their minds? Such an attempt would be vain; we do not possess\nthe philosopher's stone which would enable us to transmute one into\nanother the metals confided to us; all we can do is to work with them,\nadapting ourselves to their properties.\n\nMany children are incapable of becoming mathematicians, to whom however\nit is necessary to teach mathematics; and the mathematicians themselves\nare not all cast in the same mold. To read their works suffices to\ndistinguish among them two sorts of minds, the logicians like\nWeierstrass for example, the intuitives like Riemann. There is the same\ndifference among our students. The one sort prefer to treat their\nproblems 'by analysis' as they say, the others 'by geometry.'\n\nIt is useless to seek to change anything of that, and besides would it\nbe desirable? It is well that there are logicians and that there are\nintuitives; who would dare say whether he preferred that Weierstrass had\nnever written or that there never had been a Riemann? We must therefore\nresign ourselves to the diversity of minds, or better we must rejoice in\nit.\n\n3. Since the word understand has many meanings, the definitions which\nwill be best understood by some will not be best suited to others. We\nhave those which seek to produce an image, and those where we confine\nourselves to combining empty forms, perfectly intelligible, but purely\nintelligible, which abstraction has deprived of all matter.\n\nI know not whether it be necessary to cite examples. Let us cite them,\nanyhow, and first the definition of fractions will furnish us an extreme\ncase. In the primary schools, to define a fraction, one cuts up an apple\nor a pie; it is cut up mentally of course and not in reality, because I\ndo not suppose the budget of the primary instruction allows of such\nprodigality. At the Normal School, on the other hand, or at the college,\nit is said: a fraction is the combination of two whole numbers separated\nby a horizontal bar; we define by conventions the operations to which\nthese symbols may be submitted; it is proved that the rules of these\noperations are the same as in calculating with whole numbers, and we\nascertain finally that multiplying the fraction, according to these\nrules, by the denominator gives the numerator. This is all very well\nbecause we are addressing young people long familiarized with the notion\nof fractions through having cut up apples or other objects, and whose\nmind, matured by a hard mathematical education, has come little by\nlittle to desire a purely logical definition. But the d\u00e9butant to whom\none should try to give it, how dumfounded!\n\nSuch also are the definitions found in a book justly admired and greatly\nhonored, the _Foundations of Geometry_ by Hilbert. See in fact how he\nbegins: _We think three systems of_ THINGS _which we shall call points,\nstraights and planes_. What are these 'things'?\n\nWe know not, nor need we know; it would even be a pity to seek to know;\nall we have the right to know of them is what the assumptions tell us;\nthis for example: _Two distinct points always determine a straight_,\nwhich is followed by this remark: _in place of determine, we may say the\ntwo points are on the straight, or the straight goes through these two\npoints or joins the two points_.\n\nThus 'to be on a straight' is simply defined as synonymous with\n'determine a straight.' Behold a book of which I think much good, but\nwhich I should not recommend to a school boy. Yet I could do so without\nfear, he would not read much of it. I have taken extreme examples and no\nteacher would dream of going that far. But even stopping short of such\nmodels, does he not already expose himself to the same danger?\n\nSuppose we are in a class; the professor dictates: the circle is the\nlocus of points of the plane equidistant from an interior point called\nthe center. The good scholar writes this phrase in his note-book; the\nbad scholar draws faces; but neither understands; then the professor\ntakes the chalk and draws a circle on the board. \"Ah!\" think the\nscholars, \"why did he not say at once: a circle is a ring, we should\nhave understood.\" Doubtless the professor is right. The scholars'\ndefinition would have been of no avail, since it could serve for no\ndemonstration, since besides it would not give them the salutary habit\nof analyzing their conceptions. But one should show them that they do\nnot comprehend what they think they know, lead them to be conscious of\nthe roughness of their primitive conception, and of themselves to wish\nit purified and made precise.\n\n4. I shall return to these examples; I only wished to show you the two\nopposed conceptions; they are in violent contrast. This contrast the\nhistory of science explains. If we read a book written fifty years ago,\nmost of the reasoning we find there seems lacking in rigor. Then it was\nassumed a continuous function can change sign only by vanishing; to-day\nwe prove it. It was assumed the ordinary rules of calculation are\napplicable to incommensurable numbers; to-day we prove it. Many other\nthings were assumed which sometimes were false.\n\nWe trusted to intuition; but intuition can not give rigor, nor even\ncertainty; we see this more and more. It tells us for instance that\nevery curve has a tangent, that is to say that every continuous function\nhas a derivative, and that is false. And as we sought certainty, we had\nto make less and less the part of intuition.\n\nWhat has made necessary this evolution? We have not been slow to\nperceive that rigor could not be established in the reasonings, if it\nwere not first put into the definitions.\n\nThe objects occupying mathematicians were long ill defined; we thought\nwe knew them because we represented them with the senses or the\nimagination; but we had of them only a rough image and not a precise\nconcept upon which reasoning could take hold. It is there that the\nlogicians would have done well to direct their efforts.\n\nSo for the incommensurable number, the vague idea of continuity, which\nwe owe to intuition, has resolved itself into a complicated system of\ninequalities bearing on whole numbers. Thus have finally vanished all\nthose difficulties which frightened our fathers when they reflected upon\nthe foundations of the infinitesimal calculus. To-day only whole numbers\nare left in analysis, or systems finite or infinite of whole numbers,\nbound by a plexus of equalities and inequalities. Mathematics we say is\narithmetized.\n\n5. But do you think mathematics has attained absolute rigor without\nmaking any sacrifice? Not at all; what it has gained in rigor it has\nlost in objectivity. It is by separating itself from reality that it has\nacquired this perfect purity. We may freely run over its whole domain,\nformerly bristling with obstacles, but these obstacles have not\ndisappeared. They have only been moved to the frontier, and it would be\nnecessary to vanquish them anew if we wished to break over this frontier\nto enter the realm of the practical.\n\nWe had a vague notion, formed of incongruous elements, some _a priori_,\nothers coming from experiences more or less digested; we thought we\nknew, by intuition, its principal properties. To-day we reject the\nempiric elements, retaining only the _a priori_; one of the properties\nserves as definition and all the others are deduced from it by rigorous\nreasoning. This is all very well, but it remains to be proved that this\nproperty, which has become a definition, pertains to the real objects\nwhich experience had made known to us and whence we drew our vague\nintuitive notion. To prove that, it would be necessary to appeal to\nexperience, or to make an effort of intuition, and if we could not prove\nit, our theorems would be perfectly rigorous, but perfectly useless.\n\nLogic sometimes makes monsters. Since half a century we have seen arise\na crowd of bizarre functions which seem to try to resemble as little as\npossible the honest functions which serve some purpose. No longer\ncontinuity, or perhaps continuity, but no derivatives, etc. Nay more,\nfrom the logical point of view, it is these strange functions which are\nthe most general, those one meets without seeking no longer appear\nexcept as particular case. There remains for them only a very small\ncorner.\n\nHeretofore when a new function was invented, it was for some practical\nend; to-day they are invented expressly to put at fault the reasonings\nof our fathers, and one never will get from them anything more than\nthat.\n\nIf logic were the sole guide of the teacher, it would be necessary to\nbegin with the most general functions, that is to say with the most\nbizarre. It is the beginner that would have to be set grappling with\nthis teratologic museum. If you do not do it, the logicians might say,\nyou will achieve rigor only by stages.\n\n6. Yes, perhaps, but we can not make so cheap of reality, and I mean not\nonly the reality of the sensible world, which however has its worth,\nsince it is to combat against it that nine tenths of your students ask\nof you weapons. There is a reality more subtile, which makes the very\nlife of the mathematical beings, and which is quite other than logic.\n\nOur body is formed of cells, and the cells of atoms; are these cells and\nthese atoms then all the reality of the human body? The way these cells\nare arranged, whence results the unity of the individual, is it not also\na reality and much more interesting?\n\nA naturalist who never had studied the elephant except in the\nmicroscope, would he think he knew the animal adequately? It is the same\nin mathematics. When the logician shall have broken up each\ndemonstration into a multitude of elementary operations, all correct, he\nstill will not possess the whole reality; this I know not what which\nmakes the unity of the demonstration will completely escape him.\n\nIn the edifices built up by our masters, of what use to admire the work\nof the mason if we can not comprehend the plan of the architect? Now\npure logic can not give us this appreciation of the total effect; this\nwe must ask of intuition.\n\nTake for instance the idea of continuous function. This is at first only\na sensible image, a mark traced by the chalk on the blackboard. Little\nby little it is refined; we use it to construct a complicated system of\ninequalities, which reproduces all the features of the primitive image;\nwhen all is done, we have _removed the centering_, as after the\nconstruction of an arch; this rough representation, support thenceforth\nuseless, has disappeared and there remains only the edifice itself,\nirreproachable in the eyes of the logician. And yet, if the professor\ndid not recall the primitive image, if he did not restore momentarily\nthe _centering_, how could the student divine by what caprice all these\ninequalities have been scaffolded in this fashion one upon another? The\ndefinition would be logically correct, but it would not show him the\nveritable reality.\n\n7. So back we must return; doubtless it is hard for a master to teach\nwhat does not entirely satisfy him; but the satisfaction of the master\nis not the unique object of teaching; we should first give attention to\nwhat the mind of the pupil is and to what we wish it to become.\n\nZoologists maintain that the embryonic development of an animal\nrecapitulates in brief the whole history of its ancestors throughout\ngeologic time. It seems it is the same in the development of minds. The\nteacher should make the child go over the path his fathers trod; more\nrapidly, but without skipping stations. For this reason, the history of\nscience should be our first guide.\n\nOur fathers thought they knew what a fraction was, or continuity, or the\narea of a curved surface; we have found they did not know it. Just so\nour scholars think they know it when they begin the serious study of\nmathematics. If without warning I tell them: \"No, you do not know it;\nwhat you think you understand, you do not understand; I must prove to\nyou what seems to you evident,\" and if in the demonstration I support\nmyself upon premises which to them seem less evident than the\nconclusion, what shall the unfortunates think? They will think that the\nscience of mathematics is only an arbitrary mass of useless subtilities;\neither they will be disgusted with it, or they will play it as a game\nand will reach a state of mind like that of the Greek sophists.\n\nLater, on the contrary, when the mind of the scholar, familiarized with\nmathematical reasoning, has been matured by this long frequentation, the\ndoubts will arise of themselves and then your demonstration will be\nwelcome. It will awaken new doubts, and the questions will arise\nsuccessively to the child, as they arose successively to our fathers,\nuntil perfect rigor alone can satisfy him. To doubt everything does not\nsuffice, one must know why he doubts.\n\n8. The principal aim of mathematical teaching is to develop certain\nfaculties of the mind, and among them intuition is not the least\nprecious. It is through it that the mathematical world remains in\ncontact with the real world, and if pure mathematics could do without\nit, it would always be necessary to have recourse to it to fill up the\nchasm which separates the symbol from reality. The practician will\nalways have need of it, and for one pure geometer there should be a\nhundred practicians.\n\n\nThe engineer should receive a complete mathematical education, but for\nwhat should it serve him?\n\nTo see the different aspects of things and see them quickly; he has no\ntime to hunt mice. It is necessary that, in the complex physical objects\npresented to him, he should promptly recognize the point where the\nmathematical tools we have put in his hands can take hold. How could he\ndo it if we should leave between instruments and objects the deep chasm\nhollowed out by the logicians?\n\n9. Besides the engineers, other scholars, less numerous, are in their\nturn to become teachers; they therefore must go to the very bottom; a\nknowledge deep and rigorous of the first principles is for them before\nall indispensable. But this is no reason not to cultivate in them\nintuition; for they would get a false idea of the science if they never\nlooked at it except from a single side, and besides they could not\ndevelop in their students a quality they did not themselves possess.\n\nFor the pure geometer himself, this faculty is necessary; it is by logic\none demonstrates, by intuition one invents. To know how to criticize is\ngood, to know how to create is better. You know how to recognize if a\ncombination is correct; what a predicament if you have not the art of\nchoosing among all the possible combinations. Logic tells us that on\nsuch and such a way we are sure not to meet any obstacle; it does not\nsay which way leads to the end. For that it is necessary to see the end\nfrom afar, and the faculty which teaches us to see is intuition. Without\nit the geometer would be like a writer who should be versed in grammar\nbut had no ideas. Now how could this faculty develop if, as soon as it\nshowed itself, we chase it away and proscribe it, if we learn to set it\nat naught before knowing the good of it.\n\nAnd here permit a parenthesis to insist upon the importance of written\nexercises. Written compositions are perhaps not sufficiently emphasized\nin certain examinations, at the polytechnic school, for instance. I am\ntold they would close the door against very good scholars who have\nmastered the course, thoroughly understanding it, and who nevertheless\nare incapable of making the slightest application. I have just said the\nword understand has several meanings: such students only understand in\nthe first way, and we have seen that suffices neither to make an\nengineer nor a geometer. Well, since choice must be made, I prefer those\nwho understand completely.\n\n10. But is the art of sound reasoning not also a precious thing, which\nthe professor of mathematics ought before all to cultivate? I take good\ncare not to forget that. It should occupy our attention and from the\nvery beginning. I should be distressed to see geometry degenerate into I\nknow not what tachymetry of low grade and I by no means subscribe to the\nextreme doctrines of certain German Oberlehrer. But there are occasions\nenough to exercise the scholars in correct reasoning in the parts of\nmathematics where the inconveniences I have pointed out do not present\nthemselves. There are long chains of theorems where absolute logic has\nreigned from the very first and, so to speak, quite naturally, where the\nfirst geometers have given us models we should constantly imitate and\nadmire.\n\nIt is in the exposition of first principles that it is necessary to\navoid too much subtility; there it would be most discouraging and\nmoreover useless. We can not prove everything and we can not define\neverything; and it will always be necessary to borrow from intuition;\nwhat does it matter whether it be done a little sooner or a little\nlater, provided that in using correctly premises it has furnished us, we\nlearn to reason soundly.\n\n11. Is it possible to fulfill so many opposing conditions? Is this\npossible in particular when it is a question of giving a definition? How\nfind a concise statement satisfying at once the uncompromising rules of\nlogic, our desire to grasp the place of the new notion in the totality\nof the science, our need of thinking with images? Usually it will not be\nfound, and this is why it is not enough to state a definition; it must\nbe prepared for and justified.\n\nWhat does that mean? You know it has often been said: every definition\nimplies an assumption, since it affirms the existence of the object\ndefined. The definition then will not be justified, from the purely\nlogical point of view, until one shall have _proved_ that it involves no\ncontradiction, neither in the terms, nor with the verities previously\nadmitted.\n\nBut this is not enough; the definition is stated to us as a convention;\nbut most minds will revolt if we wish to impose it upon them as an\n_arbitrary_ convention. They will be satisfied only when you have\nanswered numerous questions.\n\nUsually mathematical definitions, as M. Liard has shown, are veritable\nconstructions built up wholly of more simple notions. But why assemble\nthese elements in this way when a thousand other combinations were\npossible?\n\nIs it by caprice? If not, why had this combination more right to exist\nthan all the others? To what need does it respond? How was it foreseen\nthat it would play an important r\u00f4le in the development of the science,\nthat it would abridge our reasonings and our calculations? Is there in\nnature some familiar object which is so to speak the rough and vague\nimage of it?\n\nThis is not all; if you answer all these questions in a satisfactory\nmanner, we shall see indeed that the new-born had the right to be\nbaptized; but neither is the choice of a name arbitrary; it is needful\nto explain by what analogies one has been guided and that if analogous\nnames have been given to different things, these things at least differ\nonly in material and are allied in form; that their properties are\nanalogous and so to say parallel.\n\nAt this cost we may satisfy all inclinations. If the statement is\ncorrect enough to please the logician, the justification will satisfy\nthe intuitive. But there is still a better procedure; wherever possible,\nthe justification should precede the statement and prepare for it; one\nshould be led on to the general statement by the study of some\nparticular examples.\n\nStill another thing: each of the parts of the statement of a definition\nhas as aim to distinguish the thing to be defined from a class of other\nneighboring objects. The definition will be understood only when you\nhave shown, not merely the object defined, but the neighboring objects\nfrom which it is proper to distinguish it, when you have given a grasp\nof the difference and when you have added explicitly: this is why in\nstating the definition I have said this or that.\n\nBut it is time to leave generalities and examine how the somewhat\nabstract principles I have expounded may be applied in arithmetic,\ngeometry, analysis and mechanics.\n\n\nARITHMETIC\n\n12. The whole number is not to be defined; in return, one ordinarily\ndefines the operations upon whole numbers; I believe the scholars learn\nthese definitions by heart and attach no meaning to them. For that there\nare two reasons: first they are made to learn them too soon, when their\nmind as yet feels no need of them; then these definitions are not\nsatisfactory from the logical point of view. A good definition for\naddition is not to be found just simply because we must stop and can not\ndefine everything. It is not defining addition to say it consists in\nadding. All that can be done is to start from a certain number of\nconcrete examples and say: the operation we have performed is called\naddition.\n\nFor subtraction it is quite otherwise; it may be logically defined as\nthe operation inverse to addition; but should we begin in that way? Here\nalso start with examples, show on these examples the reciprocity of the\ntwo operations; thus the definition will be prepared for and justified.\n\nJust so again for multiplication; take a particular problem; show that\nit may be solved by adding several equal numbers; then show that we\nreach the result more quickly by a multiplication, an operation the\nscholars already know how to do by routine and out of that the logical\ndefinition will issue naturally.\n\nDivision is defined as the operation inverse to multiplication; but\nbegin by an example taken from the familiar notion of partition and show\non this example that multiplication reproduces the dividend.\n\nThere still remain the operations on fractions. The only difficulty is\nfor multiplication. It is best to expound first the theory of\nproportion; from it alone can come a logical definition; but to make\nacceptable the definitions met at the beginning of this theory, it is\nnecessary to prepare for them by numerous examples taken from classic\nproblems of the rule of three, taking pains to introduce fractional\ndata.\n\nNeither should we fear to familiarize the scholars with the notion of\nproportion by geometric images, either by appealing to what they\nremember if they have already studied geometry, or in having recourse to\ndirect intuition, if they have not studied it, which besides will\nprepare them to study it. Finally I shall add that after defining\nmultiplication of fractions, it is needful to justify this definition by\nshowing that it is commutative, associative and distributive, and\ncalling to the attention of the auditors that this is established to\njustify the definition.\n\nOne sees what a r\u00f4le geometric images play in all this; and this r\u00f4le is\njustified by the philosophy and the history of the science. If\narithmetic had remained free from all admixture of geometry, it would\nhave known only the whole number; it is to adapt itself to the needs of\ngeometry that it invented anything else.\n\n\nGEOMETRY\n\nIn geometry we meet forthwith the notion of the straight line. Can the\nstraight line be defined? The well-known definition, the shortest path\nfrom one point to another, scarcely satisfies me. I should start simply\nwith the _ruler_ and show at first to the scholar how one may verify a\nruler by turning; this verification is the true definition of the\nstraight line; the straight line is an axis of rotation. Next he should\nbe shown how to verify the ruler by sliding and he would have one of the\nmost important properties of the straight line.\n\nAs to this other property of being the shortest path from one point to\nanother, it is a theorem which can be demonstrated apodictically, but\nthe demonstration is too delicate to find a place in secondary teaching.\nIt will be worth more to show that a ruler previously verified fits on a\nstretched thread. In presence of difficulties like these one need not\ndread to multiply assumptions, justifying them by rough experiments.\n\nIt is needful to grant these assumptions, and if one admits a few more\nof them than is strictly necessary, the evil is not very great; the\nessential thing is to learn to reason soundly on the assumptions\nadmitted. Uncle Sarcey, who loved to repeat, often said that at the\ntheater the spectator accepts willingly all the postulates imposed upon\nhim at the beginning, but the curtain once raised, he becomes\nuncompromising on the logic. Well, it is just the same in mathematics.\n\nFor the circle, we may start with the compasses; the scholars will\nrecognize at the first glance the curve traced; then make them observe\nthat the distance of the two points of the instrument remains constant,\nthat one of these points is fixed and the other movable, and so we shall\nbe led naturally to the logical definition.\n\nThe definition of the plane implies an axiom and this need not be\nhidden. Take a drawing board and show that a moving ruler may be kept\nconstantly in complete contact with this plane and yet retain three\ndegrees of freedom. Compare with the cylinder and the cone, surfaces on\nwhich an applied straight retains only two degrees of freedom; next take\nthree drawing boards; show first that they will glide while remaining\napplied to one another and this with three degrees of freedom; and\nfinally to distinguish the plane from the sphere, show that two of these\nboards which fit a third will fit each other.\n\nPerhaps you are surprised at this incessant employment of moving things;\nthis is not a rough artifice; it is much more philosophic than one would\nat first think. What is geometry for the philosopher? It is the study of\na group. And what group? That of the motions of solid bodies. How define\nthis group then without moving some solids?\n\nShould we retain the classic definition of parallels and say parallels\nare two coplanar straights which do not meet, however far they be\nprolonged? No, since this definition is negative, since it is\nunverifiable by experiment, and consequently can not be regarded as an\nimmediate datum of intuition. No, above all because it is wholly strange\nto the notion of group, to the consideration of the motion of solid\nbodies which is, as I have said, the true source of geometry. Would it\nnot be better to define first the rectilinear translation of an\ninvariable figure, as a motion wherein all the points of this figure\nhave rectilinear trajectories; to show that such a translation is\npossible by making a square glide on a ruler?\n\nFrom this experimental ascertainment, set up as an assumption, it would\nbe easy to derive the notion of parallel and Euclid's postulate itself.\n\n\n\nMECHANICS\n\nI need not return to the definition of velocity, or acceleration, or\nother kinematic notions; they may be advantageously connected with that\nof the derivative.\n\nI shall insist, on the other hand, upon the dynamic notions of force and\nmass.\n\nI am struck by one thing: how very far the young people who have\nreceived a high-school education are from applying to the real world the\nmechanical laws they have been taught. It is not only that they are\nincapable of it; they do not even think of it. For them the world of\nscience and the world of reality are separated by an impervious\npartition wall.\n\nIf we try to analyze the state of mind of our scholars, this will\nastonish us less. What is for them the real definition of force? Not\nthat which they recite, but that which, crouching in a nook of their\nmind, from there directs it wholly. Here is the definition: forces are\narrows with which one makes parallelograms. These arrows are imaginary\nthings which have nothing to do with anything existing in nature. This\nwould not happen if they had been shown forces in reality before\nrepresenting them by arrows.\n\nHow shall we define force?\n\nI think I have elsewhere sufficiently shown there is no good logical\ndefinition. There is the anthropomorphic definition, the sensation of\nmuscular effort; this is really too rough and nothing useful can be\ndrawn from it.\n\nHere is how we should go: first, to make known the genus force, we must\nshow one after the other all the species of this genus; they are very\nnumerous and very different; there is the pressure of fluids on the\ninsides of the vases wherein they are contained; the tension of threads;\nthe elasticity of a spring; the gravity working on all the molecules of\na body; friction; the normal mutual action and reaction of two solids in\ncontact.\n\nThis is only a qualitative definition; it is necessary to learn to\nmeasure force. For that begin by showing that one force may be replaced\nby another without destroying equilibrium; we may find the first example\nof this substitution in the balance and Borda's double weighing.\n\nThen show that a weight may be replaced, not only by another weight,\nbut by force of a different nature; for instance, Prony's brake permits\nreplacing weight by friction.\n\nFrom all this arises the notion of the equivalence of two forces.\n\nThe direction of a force must be defined. If a force _F_ is equivalent\nto another force _F'_ applied to the body considered by means of a\nstretched string, so that _F_ may be replaced by _F'_ without affecting\nthe equilibrium, then the point of attachment of the string will be by\ndefinition the point of application of the force _F'_, and that of the\nequivalent force _F_; the direction of the string will be the direction\nof the force _F'_ and that of the equivalent force _F_.\n\nFrom that, pass to the comparison of the magnitude of forces. If a force\ncan replace two others with the same direction, it equals their sum;\nshow for example that a weight of 20 grams may replace two 10-gram\nweights.\n\nIs this enough? Not yet. We now know how to compare the intensity of two\nforces which have the same direction and same point of application; we\nmust learn to do it when the directions are different. For that, imagine\na string stretched by a weight and passing over a pulley; we shall say\nthat the tensor of the two legs of the string is the same and equal to\nthe tension weight.\n\nThis definition of ours enables us to compare the tensions of the two\npieces of our string, and, using the preceding definitions, to compare\nany two forces having the same direction as these two pieces. It should\nbe justified by showing that the tension of the last piece of the string\nremains the same for the same tensor weight, whatever be the number and\nthe disposition of the reflecting pulleys. It has still to be completed\nby showing this is only true if the pulleys are frictionless.\n\nOnce master of these definitions, it is to be shown that the point of\napplication, the direction and the intensity suffice to determine a\nforce; that two forces for which these three elements are the same are\n_always_ equivalent and may _always_ be replaced by one another, whether\nin equilibrium or in movement, and this whatever be the other forces\nacting.\n\nIt must be shown that two concurrent forces may always be replaced by a\nunique resultant; and that _this resultant remains the same_, whether\nthe body be at rest or in motion and whatever be the other forces\napplied to it.\n\nFinally it must be shown that forces thus defined satisfy the principle\nof the equality of action and reaction.\n\nExperiment it is, and experiment alone, which can teach us all that. It\nwill suffice to cite certain common experiments, which the scholars make\ndaily without suspecting it, and to perform before them a few\nexperiments, simple and well chosen.\n\nIt is after having passed through all these meanders that one may\nrepresent forces by arrows, and I should even wish that in the\ndevelopment of the reasonings return were made from time to time from\nthe symbol to the reality. For instance it would not be difficult to\nillustrate the parallelogram of forces by aid of an apparatus formed of\nthree strings, passing over pulleys, stretched by weights and in\nequilibrium while pulling on the same point.\n\nKnowing force, it is easy to define mass; this time the definition\nshould be borrowed from dynamics; there is no way of doing otherwise,\nsince the end to be attained is to give understanding of the distinction\nbetween mass and weight. Here again, the definition should be led up to\nby experiments; there is in fact a machine which seems made expressly to\nshow what mass is, Atwood's machine; recall also the laws of the fall of\nbodies, that the acceleration of gravity is the same for heavy as for\nlight bodies, and that it varies with the latitude, etc.\n\nNow, if you tell me that all the methods I extol have long been applied\nin the schools, I shall rejoice over it more than be surprised at it. I\nknow that on the whole our mathematical teaching is good. I do not wish\nit overturned; that would even distress me. I only desire betterments\nslowly progressive. This teaching should not be subjected to brusque\noscillations under the capricious blast of ephemeral fads. In such\ntempests its high educative value would soon founder. A good and sound\nlogic should continue to be its basis. The definition by example is\nalways necessary, but it should prepare the way for the logical\ndefinition, it should not replace it; it should at least make this\nwished for, in the cases where the true logical definition can be\nadvantageously given only in advanced teaching.\n\nUnderstand that what I have here said does not imply giving up what I\nhave written elsewhere. I have often had occasion to criticize certain\ndefinitions I extol to-day. These criticisms hold good completely. These\ndefinitions can only be provisory. But it is by way of them that we must\npass.\n\n\n\n\nCHAPTER III\n\nMATHEMATICS AND LOGIC\n\n\nINTRODUCTION\n\nCan mathematics be reduced to logic without having to appeal to\nprinciples peculiar to mathematics? There is a whole school, abounding\nin ardor and full of faith, striving to prove it. They have their own\nspecial language, which is without words, using only signs. This\nlanguage is understood only by the initiates, so that commoners are\ndisposed to bow to the trenchant affirmations of the adepts. It is\nperhaps not unprofitable to examine these affirmations somewhat closely,\nto see if they justify the peremptory tone with which they are\npresented.\n\nBut to make clear the nature of the question it is necessary to enter\nupon certain historical details and in particular to recall the\ncharacter of the works of Cantor.\n\nSince long ago the notion of infinity had been introduced into\nmathematics; but this infinite was what philosophers call a _becoming_.\nThe mathematical infinite was only a quantity capable of increasing\nbeyond all limit: it was a variable quantity of which it could not be\nsaid that it _had passed_ all limits, but only that it _could pass_\nthem.\n\nCantor has undertaken to introduce into mathematics an _actual\ninfinite_, that is to say a quantity which not only is capable of\npassing all limits, but which is regarded as having already passed them.\nHe has set himself questions like these: Are there more points in space\nthan whole numbers? Are there more points in space than points in a\nplane? etc.\n\nAnd then the number of whole numbers, that of the points of space, etc.,\nconstitutes what he calls a _transfinite cardinal number_, that is to\nsay a cardinal number greater than all the ordinary cardinal numbers.\nAnd he has occupied himself in comparing these transfinite cardinal\nnumbers. In arranging in a proper order the elements of an aggregate\ncontaining an infinity of them, he has also imagined what he calls\ntransfinite ordinal numbers upon which I shall not dwell.\n\nMany mathematicians followed his lead and set a series of questions of\nthe sort. They so familiarized themselves with transfinite numbers that\nthey have come to make the theory of finite numbers depend upon that of\nCantor's cardinal numbers. In their eyes, to teach arithmetic in a way\ntruly logical, one should begin by establishing the general properties\nof transfinite cardinal numbers, then distinguish among them a very\nsmall class, that of the ordinary whole numbers. Thanks to this d\u00e9tour,\none might succeed in proving all the propositions relative to this\nlittle class (that is to say all our arithmetic and our algebra) without\nusing any principle foreign to logic. This method is evidently contrary\nto all sane psychology; it is certainly not in this way that the human\nmind proceeded in constructing mathematics; so its authors do not dream,\nI think, of introducing it into secondary teaching. But is it at least\nlogic, or, better, is it correct? It may be doubted.\n\nThe geometers who have employed it are however very numerous. They have\naccumulated formulas and they have thought to free themselves from what\nwas not pure logic by writing memoirs where the formulas no longer\nalternate with explanatory discourse as in the books of ordinary\nmathematics, but where this discourse has completely disappeared.\n\nUnfortunately they have reached contradictory results, what are called\nthe _cantorian antinomies_, to which we shall have occasion to return.\nThese contradictions have not discouraged them and they have tried to\nmodify their rules so as to make those disappear which had already shown\nthemselves, without being sure, for all that, that new ones would not\nmanifest themselves.\n\nIt is time to administer justice on these exaggerations. I do not hope\nto convince them; for they have lived too long in this atmosphere.\nBesides, when one of their demonstrations has been refuted, we are sure\nto see it resurrected with insignificant alterations, and some of them\nhave already risen several times from their ashes. Such long ago was the\nLern\u00e6an hydra with its famous heads which always grew again. Hercules\ngot through, since his hydra had only nine heads, or eleven; but here\nthere are too many, some in England, some in Germany, in Italy, in\nFrance, and he would have to give up the struggle. So I appeal only to\nmen of good judgment unprejudiced.\n\n\nI\n\nIn these latter years numerous works have been published on pure\nmathematics and the philosophy of mathematics, trying to separate and\nisolate the logical elements of mathematical reasoning. These works have\nbeen analyzed and expounded very clearly by M. Couturat in a book\nentitled: _The Principles of Mathematics_.\n\nFor M. Couturat, the new works, and in particular those of Russell and\nPeano, have finally settled the controversy, so long pending between\nLeibnitz and Kant. They have shown that there are no synthetic judgments\na priori (Kant's phrase to designate judgments which can neither be\ndemonstrated analytically, nor reduced to identities, nor established\nexperimentally), they have shown that mathematics is entirely reducible\nto logic and that intuition here plays no r\u00f4le.\n\nThis is what M. Couturat has set forth in the work just cited; this he\nsays still more explicitly in his Kant jubilee discourse, so that I\nheard my neighbor whisper: \"I well see this is the centenary of Kant's\n_death_.\"\n\nCan we subscribe to this conclusive condemnation? I think not, and I\nshall try to show why.\n\n\nII\n\nWhat strikes us first in the new mathematics is its purely formal\ncharacter: \"We think,\" says Hilbert, \"three sorts of _things_, which we\nshall call points, straights and planes. We convene that a straight\nshall be determined by two points, and that in place of saying this\nstraight is determined by these two points, we may say it passes through\nthese two points, or that these two points are situated on this\nstraight.\" What these _things_ are, not only we do not know, but we\nshould not seek to know. We have no need to, and one who never had seen\neither point or straight or plane could geometrize as well as we. That\nthe phrase _to pass through_, or the phrase _to be situated upon_ may\narouse in us no image, the first is simply a synonym of to _be\ndetermined_ and the second of _to determine_.\n\nThus, be it understood, to demonstrate a theorem, it is neither\nnecessary nor even advantageous to know what it means. The geometer\nmight be replaced by the _logic piano_ imagined by Stanley Jevons; or,\nif you choose, a machine might be imagined where the assumptions were\nput in at one end, while the theorems came out at the other, like the\nlegendary Chicago machine where the pigs go in alive and come out\ntransformed into hams and sausages. No more than these machines need the\nmathematician know what he does.\n\nI do not make this formal character of his geometry a reproach to\nHilbert. This is the way he should go, given the problem he set himself.\nHe wished to reduce to a minimum the number of the fundamental\nassumptions of geometry and completely enumerate them; now, in\nreasonings where our mind remains active, in those where intuition still\nplays a part, in living reasonings, so to speak, it is difficult not to\nintroduce an assumption or a postulate which passes unperceived. It is\ntherefore only after having carried back all the geometric reasonings to\na form purely mechanical that he could be sure of having accomplished\nhis design and finished his work.\n\nWhat Hilbert did for geometry, others have tried to do for arithmetic\nand analysis. Even if they had entirely succeeded, would the Kantians be\nfinally condemned to silence? Perhaps not, for in reducing mathematical\nthought to an empty form, it is certainly mutilated.\n\nEven admitting it were established that all the theorems could be\ndeduced by procedures purely analytic, by simple logical combinations of\na finite number of assumptions, and that these assumptions are only\nconventions; the philosopher would still have the right to investigate\nthe origins of these conventions, to see why they have been judged\npreferable to the contrary conventions.\n\nAnd then the logical correctness of the reasonings leading from the\nassumptions to the theorems is not the only thing which should occupy\nus. The rules of perfect logic, are they the whole of mathematics? As\nwell say the whole art of playing chess reduces to the rules of the\nmoves of the pieces. Among all the constructs which can be built up of\nthe materials furnished by logic, choice must be made; the true geometer\nmakes this choice judiciously because he is guided by a sure instinct,\nor by some vague consciousness of I know not what more profound and more\nhidden geometry, which alone gives value to the edifice constructed.\n\nTo seek the origin of this instinct, to study the laws of this deep\ngeometry, felt, not stated, would also be a fine employment for the\nphilosophers who do not want logic to be all. But it is not at this\npoint of view I wish to put myself, it is not thus I wish to consider\nthe question. The instinct mentioned is necessary for the inventor, but\nit would seem at first we might do without it in studying the science\nonce created. Well, what I wish to investigate is if it be true that,\nthe principles of logic once admitted, one can, I do not say discover,\nbut demonstrate, all the mathematical verities without making a new\nappeal to intuition.\n\n\nIII\n\nI once said no to this question:[12] should our reply be modified by the\nrecent works? My saying no was because \"the principle of complete\ninduction\" seemed to me at once necessary to the mathematician and\nirreducible to logic. The statement of this principle is: \"If a property\nbe true of the number 1, and if we establish that it is true of _n_ + 1\nprovided it be of _n_, it will be true of all the whole numbers.\"\nTherein I see the mathematical reasoning par excellence. I did not mean\nto say, as has been supposed, that all mathematical reasonings can be\nreduced to an application of this principle. Examining these reasonings\nclosely, we there should see applied many other analogous principles,\npresenting the same essential characteristics. In this category of\nprinciples, that of complete induction is only the simplest of all and\nthis is why I have chosen it as type.\n\n [12] See _Science and Hypothesis_, chapter I.\n\nThe current name, principle of complete induction, is not justified.\nThis mode of reasoning is none the less a true mathematical induction\nwhich differs from ordinary induction only by its certitude.\n\n\nIV\n\nDEFINITIONS AND ASSUMPTIONS\n\nThe existence of such principles is a difficulty for the uncompromising\nlogicians; how do they pretend to get out of it? The principle of\ncomplete induction, they say, is not an assumption properly so called or\na synthetic judgment _a priori_; it is just simply the definition of\nwhole number. It is therefore a simple convention. To discuss this way\nof looking at it, we must examine a little closely the relations between\ndefinitions and assumptions.\n\nLet us go back first to an article by M. Couturat on mathematical\ndefinitions which appeared in _l'Enseignement math\u00e9matique_, a magazine\npublished by Gauthier-Villars and by Georg at Geneva. We shall see there\na distinction between the _direct definition and the definition by\npostulates_.\n\n\"The definition by postulates,\" says M. Couturat, \"applies not to a\nsingle notion, but to a system of notions; it consists in enumerating\nthe fundamental relations which unite them and which enable us to\ndemonstrate all their other properties; these relations are postulates.\"\n\nIf previously have been defined all these notions but one, then this\nlast will be by definition the thing which verifies these postulates.\nThus certain indemonstrable assumptions of mathematics would be only\ndisguised definitions. This point of view is often legitimate; and I\nhave myself admitted it in regard for instance to Euclid's postulate.\n\nThe other assumptions of geometry do not suffice to completely define\ndistance; the distance then will be, by definition, among all the\nmagnitudes which satisfy these other assumptions, that which is such as\nto make Euclid's postulate true.\n\nWell the logicians suppose true for the principle of complete induction\nwhat I admit for Euclid's postulate; they want to see in it only a\ndisguised definition.\n\nBut to give them this right, two conditions must be fulfilled. Stuart\nMill says every definition implies an assumption, that by which the\nexistence of the defined object is affirmed. According to that, it\nwould no longer be the assumption which might be a disguised definition,\nit would on the contrary be the definition which would be a disguised\nassumption. Stuart Mill meant the word existence in a material and\nempirical sense; he meant to say that in defining the circle we affirm\nthere are round things in nature.\n\nUnder this form, his opinion is inadmissible. Mathematics is independent\nof the existence of material objects; in mathematics the word exist can\nhave only one meaning, it means free from contradiction. Thus rectified,\nStuart Mill's thought becomes exact; in defining a thing, we affirm that\nthe definition implies no contradiction.\n\nIf therefore we have a system of postulates, and if we can demonstrate\nthat these postulates imply no contradiction, we shall have the right to\nconsider them as representing the definition of one of the notions\nentering therein. If we can not demonstrate that, it must be admitted\nwithout proof, and that then will be an assumption; so that, seeking the\ndefinition under the postulate, we should find the assumption under the\ndefinition.\n\nUsually, to show that a definition implies no contradiction, we proceed\nby _example_, we try to make an example of a thing satisfying the\ndefinition. Take the case of a definition by postulates; we wish to\ndefine a notion _A_, and we say that, by definition, an _A_ is anything\nfor which certain postulates are true. If we can prove directly that all\nthese postulates are true of a certain object _B_, the definition will\nbe justified; the object _B_ will be an _example_ of an _A_. We shall be\ncertain that the postulates are not contradictory, since there are cases\nwhere they are all true at the same time.\n\nBut such a direct demonstration by example is not always possible.\n\nTo establish that the postulates imply no contradiction, it is then\nnecessary to consider all the propositions deducible from these\npostulates considered as premises, and to show that, among these\npropositions, no two are contradictory. If these propositions are finite\nin number, a direct verification is possible. This case is infrequent\nand uninteresting. If these propositions are infinite in number, this\ndirect verification can no longer be made; recourse must be had to\nprocedures where in general it is necessary to invoke just this\nprinciple of complete induction which is precisely the thing to be\nproved.\n\nThis is an explanation of one of the conditions the logicians should\nsatisfy, _and further on we shall see they have not done it_.\n\n\nV\n\nThere is a second. When we give a definition, it is to use it.\n\nWe therefore shall find in the sequel of the exposition the word\ndefined; have we the right to affirm, of the thing represented by this\nword, the postulate which has served for definition? Yes, evidently, if\nthe word has retained its meaning, if we do not attribute to it\nimplicitly a different meaning. Now this is what sometimes happens and\nit is usually difficult to perceive it; it is needful to see how this\nword comes into our discourse, and if the gate by which it has entered\ndoes not imply in reality a definition other than that stated.\n\nThis difficulty presents itself in all the applications of mathematics.\nThe mathematical notion has been given a definition very refined and\nvery rigorous; and for the pure mathematician all doubt has disappeared;\nbut if one wishes to apply it to the physical sciences for instance, it\nis no longer a question of this pure notion, but of a concrete object\nwhich is often only a rough image of it. To say that this object\nsatisfies, at least approximately, the definition, is to state a new\ntruth, which experience alone can put beyond doubt, and which no longer\nhas the character of a conventional postulate.\n\nBut without going beyond pure mathematics, we also meet the same\ndifficulty.\n\nYou give a subtile definition of numbers; then, once this definition\ngiven, you think no more of it; because, in reality, it is not it which\nhas taught you what number is; you long ago knew that, and when the word\nnumber further on is found under your pen, you give it the same sense as\nthe first comer. To know what is this meaning and whether it is the same\nin this phrase or that, it is needful to see how you have been led to\nspeak of number and to introduce this word into these two phrases. I\nshall not for the moment dilate upon this point, because we shall have\noccasion to return to it.\n\nThus consider a word of which we have given explicitly a definition _A_;\nafterwards in the discourse we make a use of it which implicitly\nsupposes another definition _B_. It is possible that these two\ndefinitions designate the same thing. But that this is so is a new truth\nwhich must either be demonstrated or admitted as an independent\nassumption.\n\n_We shall see farther on that the logicians have not fulfilled the\nsecond condition any better than the first._\n\n\nVI\n\nThe definitions of number are very numerous and very different; I forego\nthe enumeration even of the names of their authors. We should not be\nastonished that there are so many. If one among them was satisfactory,\nno new one would be given. If each new philosopher occupying himself\nwith this question has thought he must invent another one, this was\nbecause he was not satisfied with those of his predecessors, and he was\nnot satisfied with them because he thought he saw a petitio principii.\n\nI have always felt, in reading the writings devoted to this problem, a\nprofound feeling of discomfort; I was always expecting to run against a\npetitio principii, and when I did not immediately perceive it, I feared\nI had overlooked it.\n\nThis is because it is impossible to give a definition without using a\nsentence, and difficult to make a sentence without using a number word,\nor at least the word several, or at least a word in the plural. And then\nthe declivity is slippery and at each instant there is risk of a fall\ninto petitio principii.\n\nI shall devote my attention in what follows only to those of these\ndefinitions where the petitio principii is most ably concealed.\n\n\nVII\n\nPASIGRAPHY\n\nThe symbolic language created by Peano plays a very grand r\u00f4le in these\nnew researches. It is capable of rendering some service, but I think M.\nCouturat attaches to it an exaggerated importance which must astonish\nPeano himself.\n\nThe essential element of this language is certain algebraic signs which\nrepresent the different conjunctions: if, and, or, therefore. That these\nsigns may be convenient is possible; but that they are destined to\nrevolutionize all philosophy is a different matter. It is difficult to\nadmit that the word _if_ acquires, when written C, a virtue it had not\nwhen written if. This invention of Peano was first called _pasigraphy_,\nthat is to say the art of writing a treatise on mathematics without\nusing a single word of ordinary language. This name defined its range\nvery exactly. Later, it was raised to a more eminent dignity by\nconferring on it the title of _logistic_. This word is, it appears,\nemployed at the Military Academy, to designate the art of the\nquartermaster of cavalry, the art of marching and cantoning troops; but\nhere no confusion need be feared, and it is at once seen that this new\nname implies the design of revolutionizing logic.\n\nWe may see the new method at work in a mathematical memoir by\nBurali-Forti, entitled: _Una Questione sui numeri transfiniti_, inserted\nin Volume XI of the _Rendiconti del circolo matematico di Palermo_.\n\nI begin by saying this memoir is very interesting, and my taking it here\nas example is precisely because it is the most important of all those\nwritten in the new language. Besides, the uninitiated may read it,\nthanks to an Italian interlinear translation.\n\nWhat constitutes the importance of this memoir is that it has given the\nfirst example of those antinomies met in the study of transfinite\nnumbers and making since some years the despair of mathematicians. The\naim, says Burali-Forti, of this note is to show there may be two\ntransfinite numbers (ordinals), _a_ and _b_, such that _a_ is neither\nequal to, greater than, nor less than _b_.\n\nTo reassure the reader, to comprehend the considerations which follow,\nhe has no need of knowing what a transfinite ordinal number is.\n\nNow, Cantor had precisely proved that between two transfinite numbers as\nbetween two finite, there can be no other relation than equality or\ninequality in one sense or the other. But it is not of the substance of\nthis memoir that I wish to speak here; that would carry me much too far\nfrom my subject; I only wish to consider the form, and just to ask if\nthis form makes it gain much in rigor and whether it thus compensates\nfor the efforts it imposes upon the writer and the reader.\n\nFirst we see Burali-Forti define the number 1 as follows:\n\n 1 = [iota]T'{Ko[(n_](u, h)[epsilon](u[epsilon]Un)},\n\na definition eminently fitted to give an idea of the number 1 to persons\nwho had never heard speak of it.\n\nI understand Peanian too ill to dare risk a critique, but still I fear\nthis definition contains a petitio principii, considering that I see the\nfigure 1 in the first member and Un in letters in the second.\n\nHowever that may be, Burali-Forti starts from this definition and, after\na short calculation, reaches the equation:\n\n (27) 1[epsilon]No,\n\nwhich tells us that One is a number.\n\nAnd since we are on these definitions of the first numbers, we recall\nthat M. Couturat has also defined 0 and 1.\n\nWhat is zero? It is the number of elements of the null class. And what\nis the null class? It is that containing no element.\n\nTo define zero by null, and null by no, is really to abuse the wealth of\nlanguage; so M. Couturat has introduced an improvement in his\ndefinition, by writing:\n\n 0 = [iota][Lambda]:[phi]x = [Lambda]\u00b7[inverted c]\u00b7[Lambda]\n = (x[epsilon][phi]x),\n\nwhich means: zero is the number of things satisfying a condition never\nsatisfied.\n\nBut as never means _in no case_ I do not see that the progress is great.\n\nI hasten to add that the definition M. Couturat gives of the number 1 is\nmore satisfactory.\n\nOne, says he in substance, is the number of elements in a class in which\nany two elements are identical.\n\nIt is more satisfactory, I have said, in this sense that to define 1, he\ndoes not use the word one; in compensation, he uses the word two. But I\nfear, if asked what is two, M. Couturat would have to use the word one.\n\n\n\nVIII\n\nBut to return to the memoir of Burali-Forti; I have said his conclusions\nare in direct opposition to those of Cantor. Now, one day M. Hadamard\ncame to see me and the talk fell upon this antinomy.\n\n\"Burali-Forti's reasoning,\" I said, \"does it not seem to you\nirreproachable?\" \"No, and on the contrary I find nothing to object to in\nthat of Cantor. Besides, Burali-Forti had no right to speak of the\naggregate of _all_ the ordinal numbers.\"\n\n\"Pardon, he had the right, since he could always put\n\n [Omega] = T'(No,[epsilon]>).\n\nI should like to know who was to prevent him, and can it be said a thing\ndoes not exist, when we have called it [Omega]?\"\n\nIt was in vain, I could not convince him (which besides would have been\nsad, since he was right). Was it merely because I do not speak the\nPeanian with enough eloquence? Perhaps; but between ourselves I do not\nthink so.\n\nThus, despite all this pasigraphic apparatus, the question was not\nsolved. What does that prove? In so far as it is a question only of\nproving one a number, pasigraphy suffices, but if a difficulty presents\nitself, if there is an antinomy to solve, pasigraphy becomes impotent.\n\n\n\n\nCHAPTER IV\n\nTHE NEW LOGICS\n\n\nI\n\n_The Russell Logic_\n\nTo justify its pretensions, logic had to change. We have seen new logics\narise of which the most interesting is that of Russell. It seems he has\nnothing new to write about formal logic, as if Aristotle there had\ntouched bottom. But the domain Russell attributes to logic is infinitely\nmore extended than that of the classic logic, and he has put forth on\nthe subject views which are original and at times well warranted.\n\nFirst, Russell subordinates the logic of classes to that of\npropositions, while the logic of Aristotle was above all the logic of\nclasses and took as its point of departure the relation of subject to\npredicate. The classic syllogism, \"Socrates is a man,\" etc., gives place\nto the hypothetical syllogism: \"If _A_ is true, _B_ is true; now if _B_\nis true, _C_ is true,\" etc. And this is, I think, a most happy idea,\nbecause the classic syllogism is easy to carry back to the hypothetical\nsyllogism, while the inverse transformation is not without difficulty.\n\nAnd then this is not all. Russell's logic of propositions is the study\nof the laws of combination of the conjunctions _if_, _and_, _or_, and\nthe negation _not_.\n\nIn adding here two other conjunctions, _and_ and _or_, Russell opens to\nlogic a new field. The symbols _and_, _or_ follow the same laws as the\ntwo signs \u00d7 and +, that is to say the commutative associative and\ndistributive laws. Thus _and_ represents logical multiplication, while\n_or_ represents logical addition. This also is very interesting.\n\nRussell reaches the conclusion that any false proposition implies all\nother propositions true or false. M. Couturat says this conclusion will\nat first seem paradoxical. It is sufficient however to have corrected a\nbad thesis in mathematics to recognize how right Russell is. The\ncandidate often is at great pains to get the first false equation; but\nthat once obtained, it is only sport then for him to accumulate the most\nsurprising results, some of which even may be true.\n\n\nII\n\nWe see how much richer the new logic is than the classic logic; the\nsymbols are multiplied and allow of varied combinations _which are no\nlonger limited in number_. Has one the right to give this extension to\nthe meaning of the word _logic_? It would be useless to examine this\nquestion and to seek with Russell a mere quarrel about words. Grant him\nwhat he demands; but be not astonished if certain verities declared\nirreducible to logic in the old sense of the word find themselves now\nreducible to logic in the new sense--something very different.\n\nA great number of new notions have been introduced, and these are not\nsimply combinations of the old. Russell knows this, and not only at the\nbeginning of the first chapter, 'The Logic of Propositions,' but at the\nbeginning of the second and third, 'The Logic of Classes' and 'The Logic\nof Relations,' he introduces new words that he declares indefinable.\n\nAnd this is not all; he likewise introduces principles he declares\nindemonstrable. But these indemonstrable principles are appeals to\nintuition, synthetic judgments _a priori_. We regard them as intuitive\nwhen we meet them more or less explicitly enunciated in mathematical\ntreatises; have they changed character because the meaning of the word\nlogic has been enlarged and we now find them in a book entitled\n_Treatise on Logic_? _They have not changed nature; they have only\nchanged place._\n\n\nIII\n\nCould these principles be considered as disguised definitions? It would\nthen be necessary to have some way of proving that they imply no\ncontradiction. It would be necessary to establish that, however far one\nfollowed the series of deductions, he would never be exposed to\ncontradicting himself.\n\nWe might attempt to reason as follows: We can verify that the\noperations of the new logic applied to premises exempt from\ncontradiction can only give consequences equally exempt from\ncontradiction. If therefore after _n_ operations we have not met\ncontradiction, we shall not encounter it after _n_ + 1. Thus it is\nimpossible that there should be a moment when contradiction _begins_,\nwhich shows we shall never meet it. Have we the right to reason in this\nway? No, for this would be to make use of complete induction; and\n_remember, we do not yet know the principle of complete induction_.\n\nWe therefore have not the right to regard these assumptions as disguised\ndefinitions and only one resource remains for us, to admit a new act of\nintuition for each of them. Moreover I believe this is indeed the\nthought of Russell and M. Couturat.\n\nThus each of the nine indefinable notions and of the twenty\nindemonstrable propositions (I believe if it were I that did the\ncounting, I should have found some more) which are the foundation of the\nnew logic, logic in the broad sense, presupposes a new and independent\nact of our intuition and (why not say it?) a veritable synthetic\njudgment _a priori_. On this point all seem agreed, but what Russell\nclaims, and _what seems to me doubtful, is that after these appeals to\nintuition, that will be the end of it; we need make no others and can\nbuild all mathematics without the intervention of any new element_.\n\n\nIV\n\nM. Couturat often repeats that this new logic is altogether independent\nof the idea of number. I shall not amuse myself by counting how many\nnumeral adjectives his exposition contains, both cardinal and ordinal,\nor indefinite adjectives such as several. We may cite, however, some\nexamples:\n\n\"The logical product of _two_ or _more_ propositions is....\";\n\n\"All propositions are capable only of _two_ values, true and false\";\n\n\"The relative product of _two_ relations is a relation\";\n\n\"A relation exists between two terms,\" etc., etc.\n\nSometimes this inconvenience would not be unavoidable, but sometimes\nalso it is essential. A relation is incomprehensible without two terms;\nit is impossible to have the intuition of the relation, without having\nat the same time that of its two terms, and without noticing they are\ntwo, because, if the relation is to be conceivable, it is necessary that\nthere be two and only two.\n\n\nV\n\n_Arithmetic_\n\nI reach what M. Couturat calls the _ordinal theory_ which is the\nfoundation of arithmetic properly so called. M. Couturat begins by\nstating Peano's five assumptions, which are independent, as has been\nproved by Peano and Padoa.\n\n1. Zero is an integer.\n\n2. Zero is not the successor of any integer.\n\n3. The successor of an integer is an integer. To this it would be proper\nto add,\n\nEvery integer has a successor.\n\n4. Two integers are equal if their successors are.\n\nThe fifth assumption is the principle of complete induction.\n\nM. Couturat considers these assumptions as disguised definitions; they\nconstitute the definition by postulates of zero, of successor, and of\ninteger.\n\nBut we have seen that for a definition by postulates to be acceptable we\nmust be able to prove that it implies no contradiction.\n\nIs this the case here? Not at all.\n\nThe demonstration can not be made _by example_. We can not take a part\nof the integers, for instance the first three, and prove they satisfy\nthe definition.\n\nIf I take the series 0, 1, 2, I see it fulfils the assumptions 1, 2, 4\nand 5; but to satisfy assumption 3 it still is necessary that 3 be an\ninteger, and consequently that the series 0, 1, 2, 3, fulfil the\nassumptions; we might prove that it satisfies assumptions 1, 2, 4, 5,\nbut assumption 3 requires besides that 4 be an integer and that the\nseries 0, 1, 2, 3, 4 fulfil the assumptions, and so on.\n\nIt is therefore impossible to demonstrate the assumptions for certain\nintegers without proving them for all; we must give up proof by\nexample.\n\nIt is necessary then to take all the consequences of our assumptions and\nsee if they contain no contradiction.\n\nIf these consequences were finite in number, this would be easy; but\nthey are infinite in number; they are the whole of mathematics, or at\nleast all arithmetic.\n\nWhat then is to be done? Perhaps strictly we could repeat the reasoning\nof number III.\n\nBut as we have said, this reasoning is complete induction, and it is\nprecisely the principle of complete induction whose justification would\nbe the point in question.\n\n\nVI\n\n_The Logic of Hilbert_\n\nI come now to the capital work of Hilbert which he communicated to the\nCongress of Mathematicians at Heidelberg, and of which a French\ntranslation by M. Pierre Boutroux appeared in _l'Enseignement\nmath\u00e9matique_, while an English translation due to Halsted appeared in\n_The Monist_.[13] In this work, which contains profound thoughts, the\nauthor's aim is analogous to that of Russell, but on many points he\ndiverges from his predecessor.\n\n [13] 'The Foundations of Logic and Arithmetic,' _Monist_, XV.,\n 338-352.\n\n\"But,\" he says (_Monist_, p. 340), \"on attentive consideration we become\naware that in the usual exposition of the laws of logic certain\nfundamental concepts of arithmetic are already employed; for example,\nthe concept of the aggregate, in part also the concept of number.\n\n\"We fall thus into a vicious circle and therefore to avoid paradoxes a\npartly simultaneous development of the laws of logic and arithmetic is\nrequisite.\"\n\nWe have seen above that what Hilbert says of the principles of logic _in\nthe usual exposition_ applies likewise to the logic of Russell. So for\nRussell logic is prior to arithmetic; for Hilbert they are\n'simultaneous.' We shall find further on other differences still\ngreater, but we shall point them out as we come to them. I prefer to\nfollow step by step the development of Hilbert's thought, quoting\ntextually the most important passages.\n\n\"Let us take as the basis of our consideration first of all a\nthought-thing 1 (one)\" (p. 341). Notice that in so doing we in no wise\nimply the notion of number, because it is understood that 1 is here only\na symbol and that we do not at all seek to know its meaning. \"The taking\nof this thing together with itself respectively two, three or more\ntimes....\" Ah! this time it is no longer the same; if we introduce the\nwords 'two,' 'three,' and above all 'more,' 'several,' we introduce the\nnotion of number; and then the definition of finite whole number which\nwe shall presently find, will come too late. Our author was too\ncircumspect not to perceive this begging of the question. So at the end\nof his work he tries to proceed to a truly patching-up process.\n\nHilbert then introduces two simple objects 1 and =, and considers all\nthe combinations of these two objects, all the combinations of their\ncombinations, etc. It goes without saying that we must forget the\nordinary meaning of these two signs and not attribute any to them.\n\nAfterwards he separates these combinations into two classes, the class\nof the existent and the class of the non-existent, and till further\norders this separation is entirely arbitrary. Every affirmative\nstatement tells us that a certain combination belongs to the class of\nthe existent; every negative statement tells us that a certain\ncombination belongs to the class of the non-existent.\n\n\nVII\n\nNote now a difference of the highest importance. For Russell any object\nwhatsoever, which he designates by _x_, is an object absolutely\nundetermined and about which he supposes nothing; for Hilbert it is one\nof the combinations formed with the symbols 1 and =; he could not\nconceive of the introduction of anything other than combinations of\nobjects already defined. Moreover Hilbert formulates his thought in the\nneatest way, and I think I must reproduce _in extenso_ his statement (p.\n348):\n\n\"In the assumptions the arbitraries (as equivalent for the concept\n'every' and 'all' in the customary logic) represent only those\nthought-things and their combinations with one another, which at this\nstage are laid down as fundamental or are to be newly defined.\nTherefore in the deduction of inferences from the assumptions, the\narbitraries, which occur in the assumptions, can be replaced only by\nsuch thought-things and their combinations.\n\n\"Also we must duly remember, that through the super-addition and making\nfundamental of a new thought-thing the preceding assumptions undergo an\nenlargement of their validity, and where necessary, are to be subjected\nto a change in conformity with the sense.\"\n\nThe contrast with Russell's view-point is complete. For this philosopher\nwe may substitute for _x_ not only objects already known, but anything.\n\nRussell is faithful to his point of view, which is that of\ncomprehension. He starts from the general idea of being, and enriches it\nmore and more while restricting it, by adding new qualities. Hilbert on\nthe contrary recognizes as possible beings only combinations of objects\nalready known; so that (looking at only one side of his thought) we\nmight say he takes the view-point of extension.\n\n\nVIII\n\nLet us continue with the exposition of Hilbert's ideas. He introduces\ntwo assumptions which he states in his symbolic language but which\nsignify, in the language of the uninitiated, that every quality is equal\nto itself and that every operation performed upon two identical\nquantities gives identical results.\n\nSo stated, they are evident, but thus to present them would be to\nmisrepresent Hilbert's thought. For him mathematics has to combine only\npure symbols, and a true mathematician should reason upon them without\npreconceptions as to their meaning. So his assumptions are not for him\nwhat they are for the common people.\n\nHe considers them as representing the definition by postulates of the\nsymbol (=) heretofore void of all signification. But to justify this\ndefinition we must show that these two assumptions lead to no\ncontradiction. For this Hilbert used the reasoning of our number III,\nwithout appearing to perceive that he is using complete induction.\n\n\nIX\n\nThe end of Hilbert's memoir is altogether enigmatic and I shall not lay\nstress upon it. Contradictions accumulate; we feel that the author is\ndimly conscious of the _petitio principii_ he has committed, and that he\nseeks vainly to patch up the holes in his argument.\n\nWhat does this mean? At the point of proving that the definition of the\nwhole number by the assumption of complete induction implies no\ncontradiction, Hilbert withdraws as Russell and Couturat withdrew,\nbecause the difficulty is too great.\n\n\nX\n\n_Geometry_\n\nGeometry, says M. Couturat, is a vast body of doctrine wherein the\nprinciple of complete induction does not enter. That is true in a\ncertain measure; we can not say it is entirely absent, but it enters\nvery slightly. If we refer to the _Rational Geometry_ of Dr. Halsted\n(New York, John Wiley and Sons, 1904) built up in accordance with the\nprinciples of Hilbert, we see the principle of induction enter for the\nfirst time on page 114 (unless I have made an oversight, which is quite\npossible).[14]\n\n [14] Second ed., 1907, p. 86; French ed., 1911, p. 97. G. B. H.\n\nSo geometry, which only a few years ago seemed the domain where the\nreign of intuition was uncontested, is to-day the realm where the\nlogicians seem to triumph. Nothing could better measure the importance\nof the geometric works of Hilbert and the profound impress they have\nleft on our conceptions.\n\nBut be not deceived. What is after all the fundamental theorem of\ngeometry? It is that the assumptions of geometry imply no contradiction,\nand this we can not prove without the principle of induction.\n\nHow does Hilbert demonstrate this essential point? By leaning upon\nanalysis and through it upon arithmetic and through it upon the\nprinciple of induction.\n\nAnd if ever one invents another demonstration, it will still be\nnecessary to lean upon this principle, since the possible consequences\nof the assumptions, of which it is necessary to show that they are not\ncontradictory, are infinite in number.\n\n\nXI\n\n_Conclusion_\n\nOur conclusion straightway is that the principle of induction can not be\nregarded as the disguised definition of the entire world.\n\nHere are three truths: (1) The principle of complete induction; (2)\nEuclid's postulate; (3) the physical law according to which phosphorus\nmelts at 44\u00b0 (cited by M. Le Roy).\n\nThese are said to be three disguised definitions: the first, that of the\nwhole number; the second, that of the straight line; the third, that of\nphosphorus.\n\nI grant it for the second; I do not admit it for the other two. I must\nexplain the reason for this apparent inconsistency.\n\nFirst, we have seen that a definition is acceptable only on condition\nthat it implies no contradiction. We have shown likewise that for the\nfirst definition this demonstration is impossible; on the other hand, we\nhave just recalled that for the second Hilbert has given a complete\nproof.\n\nAs to the third, evidently it implies no contradiction. Does this mean\nthat the definition guarantees, as it should, the existence of the\nobject defined? We are here no longer in the mathematical sciences, but\nin the physical, and the word existence has no longer the same meaning.\nIt no longer signifies absence of contradiction; it means objective\nexistence.\n\nYou already see a first reason for the distinction I made between the\nthree cases; there is a second. In the applications we have to make of\nthese three concepts, do they present themselves to us as defined by\nthese three postulates?\n\nThe possible applications of the principle of induction are innumerable;\ntake, for example, one of those we have expounded above, and where it is\nsought to prove that an aggregate of assumptions can lead to no\ncontradiction. For this we consider one of the series of syllogisms we\nmay go on with in starting from these assumptions as premises. When we\nhave finished the _n_th syllogism, we see we can make still another and\nthis is the _n_ + 1th. Thus the number _n_ serves to count a series of\nsuccessive operations; it is a number obtainable by successive\nadditions. This therefore is a number from which we may go back to\nunity by _successive subtractions_. Evidently we could not do this if we\nhad _n_ = _n_ - 1, since then by subtraction we should always obtain\nagain the same number. So the way we have been led to consider this\nnumber _n_ implies a definition of the finite whole number and this\ndefinition is the following: A finite whole number is that which can be\nobtained by successive additions; it is such that _n_ is not equal to\n_n_ - 1.\n\nThat granted, what do we do? We show that if there has been no\ncontradiction up to the _n_th syllogism, no more will there be up to the\n_n_ + 1th, and we conclude there never will be. You say: I have the\nright to draw this conclusion, since the whole numbers are by definition\nthose for which a like reasoning is legitimate. But that implies another\ndefinition of the whole number, which is as follows: A whole number is\nthat on which we may reason by recurrence. In the particular case it is\nthat of which we may say that, if the absence of contradiction up to the\ntime of a syllogism of which the number is an integer carries with it\nthe absence of contradiction up to the time of the syllogism whose\nnumber is the following integer, we need fear no contradiction for any\nof the syllogisms whose number is an integer.\n\nThe two definitions are not identical; they are doubtless equivalent,\nbut only in virtue of a synthetic judgment _a priori_; we can not pass\nfrom one to the other by a purely logical procedure. Consequently we\nhave no right to adopt the second, after having introduced the whole\nnumber by a way that presupposes the first.\n\nOn the other hand, what happens with regard to the straight line? I have\nalready explained this so often that I hesitate to repeat it again, and\nshall confine myself to a brief recapitulation of my thought. We have\nnot, as in the preceding case, two equivalent definitions logically\nirreducible one to the other. We have only one expressible in words.\nWill it be said there is another which we feel without being able to\nword it, since we have the intuition of the straight line or since we\nrepresent to ourselves the straight line? First of all, we can not\nrepresent it to ourselves in geometric space, but only in representative\nspace, and then we can represent to ourselves just as well the objects\nwhich possess the other properties of the straight line, save that of\nsatisfying Euclid's postulate. These objects are 'the non-Euclidean\nstraights,' which from a certain point of view are not entities void of\nsense, but circles (true circles of true space) orthogonal to a certain\nsphere. If, among these objects equally capable of representation, it is\nthe first (the Euclidean straights) which we call straights, and not the\nlatter (the non-Euclidean straights), this is properly by definition.\n\nAnd arriving finally at the third example, the definition of phosphorus,\nwe see the true definition would be: Phosphorus is the bit of matter I\nsee in yonder flask.\n\n\nXII\n\nAnd since I am on this subject, still another word. Of the phosphorus\nexample I said: \"This proposition is a real verifiable physical law,\nbecause it means that all bodies having all the other properties of\nphosphorus, save its point of fusion, melt like it at 44\u00b0.\" And it was\nanswered: \"No, this law is not verifiable, because if it were shown that\ntwo bodies resembling phosphorus melt one at 44\u00b0 and the other at 50\u00b0,\nit might always be said that doubtless, besides the point of fusion,\nthere is some other unknown property by which they differ.\"\n\nThat was not quite what I meant to say. I should have written, \"All\nbodies possessing such and such properties finite in number (to wit, the\nproperties of phosphorus stated in the books on chemistry, the\nfusion-point excepted) melt at 44\u00b0.\"\n\nAnd the better to make evident the difference between the case of the\nstraight and that of phosphorus, one more remark. The straight has in\nnature many images more or less imperfect, of which the chief are the\nlight rays and the rotation axis of the solid. Suppose we find the ray\nof light does not satisfy Euclid's postulate (for example by showing\nthat a star has a negative parallax), what shall we do? Shall we\nconclude that the straight being by definition the trajectory of light\ndoes not satisfy the postulate, or, on the other hand, that the straight\nby definition satisfying the postulate, the ray of light is not\nstraight?\n\nAssuredly we are free to adopt the one or the other definition and\nconsequently the one or the other conclusion; but to adopt the first\nwould be stupid, because the ray of light probably satisfies only\nimperfectly not merely Euclid's postulate, but the other properties of\nthe straight line, so that if it deviates from the Euclidean straight,\nit deviates no less from the rotation axis of solids which is another\nimperfect image of the straight line; while finally it is doubtless\nsubject to change, so that such a line which yesterday was straight will\ncease to be straight to-morrow if some physical circumstance has\nchanged.\n\nSuppose now we find that phosphorus does not melt at 44\u00b0, but at 43.9\u00b0.\nShall we conclude that phosphorus being by definition that which melts\nat 44\u00b0, this body that we did call phosphorus is not true phosphorus,\nor, on the other hand, that phosphorous melts at 43.9\u00b0? Here again we\nare free to adopt the one or the other definition and consequently the\none or the other conclusion; but to adopt the first would be stupid\nbecause we can not be changing the name of a substance every time we\ndetermine a new decimal of its fusion-point.\n\n\nXIII\n\nTo sum up, Russell and Hilbert have each made a vigorous effort; they\nhave each written a work full of original views, profound and often well\nwarranted. These two works give us much to think about and we have much\nto learn from them. Among their results, some, many even, are solid and\ndestined to live.\n\nBut to say that they have finally settled the debate between Kant and\nLeibnitz and ruined the Kantian theory of mathematics is evidently\nincorrect. I do not know whether they really believed they had done it,\nbut if they believed so, they deceived themselves.\n\n\n\n\nCHAPTER V\n\nTHE LATEST EFFORTS OF THE LOGISTICIANS\n\n\nI\n\nThe logicians have attempted to answer the preceding considerations. For\nthat, a transformation of logistic was necessary, and Russell in\nparticular has modified on certain points his original views. Without\nentering into the details of the debate, I should like to return to the\ntwo questions to my mind most important: Have the rules of logistic\ndemonstrated their fruitfulness and infallibility? Is it true they\nafford means of proving the principle of complete induction without any\nappeal to intuition?\n\n\nII\n\n_The Infallibility of Logistic_\n\nOn the question of fertility, it seems M. Couturat has na\u00efve illusions.\nLogistic, according to him, lends invention 'stilts and wings,' and on\nthe next page: \"_Ten years ago_, Peano published the first edition of\nhis _Formulaire_.\" How is that, ten years of wings and not to have\nflown!\n\nI have the highest esteem for Peano, who has done very pretty things\n(for instance his 'space-filling curve,' a phrase now discarded); but\nafter all he has not gone further nor higher nor quicker than the\nmajority of wingless mathematicians, and would have done just as well\nwith his legs.\n\nOn the contrary I see in logistic only shackles for the inventor. It is\nno aid to conciseness--far from it, and if twenty-seven equations were\nnecessary to establish that 1 is a number, how many would be needed to\nprove a real theorem? If we distinguish, with Whitehead, the individual\n_x_, the class of which the only member is _x_ and which shall be called\n[iota]_x_, then the class of which the only member is the class of which\nthe only member is _x_ and which shall be called [mu]_x_, do you think\nthese distinctions, useful as they may be, go far to quicken our pace?\n\nLogistic forces us to say all that is ordinarily left to be understood;\nit makes us advance step by step; this is perhaps surer but not quicker.\n\nIt is not wings you logisticians give us, but leading-strings. And then\nwe have the right to require that these leading-strings prevent our\nfalling. This will be their only excuse. When a bond does not bear much\ninterest, it should at least be an investment for a father of a family.\n\nShould your rules be followed blindly? Yes, else only intuition could\nenable us to distinguish among them; but then they must be infallible;\nfor only in an infallible authority can one have a blind confidence.\nThis, therefore, is for you a necessity. Infallible you shall be, or not\nat all.\n\nYou have no right to say to us: \"It is true we make mistakes, but so do\nyou.\" For us to blunder is a misfortune, a very great misfortune; for\nyou it is death.\n\nNor may you ask: Does the infallibility of arithmetic prevent errors in\naddition? The rules of calculation are infallible, and yet we see those\nblunder _who do not apply these rules_; but in checking their\ncalculation it is at once seen where they went wrong. Here it is not at\nall the case; the logicians _have applied_ their rules, and they have\nfallen into contradiction; and so true is this, that they are preparing\nto change these rules and to \"sacrifice the notion of class.\" Why change\nthem if they were infallible?\n\n\"We are not obliged,\" you say, \"to solve _hic et nunc_ all possible\nproblems.\" Oh, we do not ask so much of you. If, in face of a problem,\nyou would give _no_ solution, we should have nothing to say; but on the\ncontrary you give us _two_ of them and those contradictory, and\nconsequently at least one false; this it is which is failure.\n\nRussell seeks to reconcile these contradictions, which can only be done,\naccording to him, \"by restricting or even sacrificing the notion of\nclass.\" And M. Couturat, discovering the success of his attempt, adds:\n\"If the logicians succeed where others have failed, M. Poincar\u00e9 will\nremember this phrase, and give the honor of the solution to logistic.\"\n\nBut no! Logistic exists, it has its code which has already had four\neditions; or rather this code is logistic itself. Is Mr. Russell\npreparing to show that one at least of the two contradictory reasonings\nhas transgressed the code? Not at all; he is preparing to change these\nlaws and to abrogate a certain number of them. If he succeeds, I shall\ngive the honor of it to Russell's intuition and not to the Peanian\nlogistic which he will have destroyed.\n\n\nIII\n\n_The Liberty of Contradiction_\n\nI made two principal objections to the definition of whole number\nadopted in logistic. What says M. Couturat to the first of these\nobjections?\n\nWhat does the word _exist_ mean in mathematics? It means, I said, to be\nfree from contradiction. This M. Couturat contests. \"Logical existence,\"\nsays he, \"is quite another thing from the absence of contradiction. It\nconsists in the fact that a class is not empty.\" To say: _a_'s exist,\nis, by definition, to affirm that the class _a_ is not null.\n\nAnd doubtless to affirm that the class _a_ is not null, is, by\ndefinition, to affirm that _a_'s exist. But one of the two affirmations\nis as denuded of meaning as the other, if they do not both signify,\neither that one may see or touch _a_'s which is the meaning physicists\nor naturalists give them, or that one may conceive an _a_ without being\ndrawn into contradictions, which is the meaning given them by logicians\nand mathematicians.\n\nFor M. Couturat, \"it is not non-contradiction that proves existence, but\nit is existence that proves non-contradiction.\" To establish the\nexistence of a class, it is necessary therefore to establish, by an\n_example_, that there is an individual belonging to this class: \"But, it\nwill be said, how is the existence of this individual proved? Must not\nthis existence be established, in order that the existence of the class\nof which it is a part may be deduced? Well, no; however paradoxical may\nappear the assertion, we never demonstrate the existence of an\nindividual. Individuals, just because they are individuals, are always\nconsidered as existent.... We never have to express that an individual\nexists, absolutely speaking, but only that it exists in a class.\" M.\nCouturat finds his own assertion paradoxical, and he will certainly not\nbe the only one. Yet it must have a meaning. It doubtless means that the\nexistence of an individual, alone in the world, and of which nothing is\naffirmed, can not involve contradiction; in so far as it is all alone it\nevidently will not embarrass any one. Well, so let it be; we shall admit\nthe existence of the individual, 'absolutely speaking,' but nothing\nmore. It remains to prove the existence of the individual 'in a class,'\nand for that it will always be necessary to prove that the affirmation,\n\"Such an individual belongs to such a class,\" is neither contradictory\nin itself, nor to the other postulates adopted.\n\n\"It is then,\" continues M. Couturat, \"arbitrary and misleading to\nmaintain that a definition is valid only if we first prove it is not\ncontradictory.\" One could not claim in prouder and more energetic terms\nthe liberty of contradiction. \"In any case, the _onus probandi_ rests\nupon those who believe that these principles are contradictory.\"\nPostulates are presumed to be compatible until the contrary is proved,\njust as the accused person is presumed innocent. Needless to add that I\ndo not assent to this claim. But, you say, the demonstration you require\nof us is impossible, and you can not ask us to jump over the moon.\nPardon me; that is impossible for you, but not for us, who admit the\nprinciple of induction as a synthetic judgment _a priori_. And that\nwould be necessary for you, as for us.\n\nTo demonstrate that a system of postulates implies no contradiction, it\nis necessary to apply the principle of complete induction; this mode of\nreasoning not only has nothing 'bizarre' about it, but it is the only\ncorrect one. It is not 'unlikely' that it has ever been employed; and it\nis not hard to find 'examples and precedents' of it. I have cited two\nsuch instances borrowed from Hilbert's article. He is not the only one\nto have used it, and those who have not done so have been wrong. What I\nhave blamed Hilbert for is not his having recourse to it (a born\nmathematician such as he could not fail to see a demonstration was\nnecessary and this the only one possible), but his having recourse\nwithout recognizing the reasoning by recurrence.\n\n\nIV\n\n_The Second Objection_\n\nI pointed out a second error of logistic in Hilbert's article. To-day\nHilbert is excommunicated and M. Couturat no longer regards him as of\nthe logistic cult; so he asks if I have found the same fault among the\northodox. No, I have not seen it in the pages I have read; I know not\nwhether I should find it in the three hundred pages they have written\nwhich I have no desire to read.\n\nOnly, they must commit it the day they wish to make any application of\nmathematics. This science has not as sole object the eternal\ncontemplation of its own navel; it has to do with nature and some day it\nwill touch it. Then it will be necessary to shake off purely verbal\ndefinitions and to stop paying oneself with words.\n\nTo go back to the example of Hilbert: always the point at issue is\nreasoning by recurrence and the question of knowing whether a system of\npostulates is not contradictory. M. Couturat will doubtless say that\nthen this does not touch him, but it perhaps will interest those who do\nnot claim, as he does, the liberty of contradiction.\n\nWe wish to establish, as above, that we shall never encounter\ncontradiction after any number of deductions whatever, provided this\nnumber be finite. For that, it is necessary to apply the principle of\ninduction. Should we here understand by finite number every number to\nwhich by definition the principle of induction applies? Evidently not,\nelse we should be led to most embarrassing consequences. To have the\nright to lay down a system of postulates, we must be sure they are not\ncontradictory. This is a truth admitted by _most_ scientists; I should\nhave written _by all_ before reading M. Couturat's last article. But\nwhat does this signify? Does it mean that we must be sure of not meeting\ncontradiction after a _finite_ number of propositions, the _finite_\nnumber being by definition that which has all properties of recurrent\nnature, so that if one of these properties fails--if, for instance, we\ncome upon a contradiction--we shall agree to say that the number in\nquestion is not finite? In other words, do we mean that we must be sure\nnot to meet contradictions, on condition of agreeing to stop just when\nwe are about to encounter one? To state such a proposition is enough to\ncondemn it.\n\nSo, Hilbert's reasoning not only assumes the principle of induction, but\nit supposes that this principle is given us not as a simple definition,\nbut as a synthetic judgment _a priori_.\n\nTo sum up:\n\nA demonstration is necessary.\n\nThe only demonstration possible is the proof by recurrence.\n\nThis is legitimate only if we admit the principle of induction and if we\nregard it not as a definition but as a synthetic judgment.\n\n\nV\n\n_The Cantor Antinomies_\n\nNow to examine Russell's new memoir. This memoir was written with the\nview to conquer the difficulties raised by those Cantor antinomies to\nwhich frequent allusion has already been made. Cantor thought he could\nconstruct a science of the infinite; others went on in the way he\nopened, but they soon ran foul of strange contradictions. These\nantinomies are already numerous, but the most celebrated are:\n\n1. The Burali-Forti antinomy;\n\n2. The Zermelo-K\u00f6nig antinomy;\n\n3. The Richard antinomy.\n\nCantor proved that the ordinal numbers (the question is of transfinite\nordinal numbers, a new notion introduced by him) can be ranged in a\nlinear series; that is to say that of two unequal ordinals one is always\nless than the other. Burali-Forti proves the contrary; and in fact he\nsays in substance that if one could range _all_ the ordinals in a linear\nseries, this series would define an ordinal greater than _all_ the\nothers; we could afterwards adjoin 1 and would obtain again an ordinal\nwhich would be _still greater_, and this is contradictory.\n\nWe shall return later to the Zermelo-K\u00f6nig antinomy which is of a\nslightly different nature. The Richard antinomy[15] is as follows:\nConsider all the decimal numbers definable by a finite number of words;\nthese decimal numbers form an aggregate _E_, and it is easy to see that\nthis aggregate is countable, that is to say we can _number_ the\ndifferent decimal numbers of this assemblage from 1 to infinity. Suppose\nthe numbering effected, and define a number _N_ as follows: If the _n_th\ndecimal of the _n_th number of the assemblage _E_ is\n\n 0, 1, 2, 3, 4, 5, 6, 7, 8, 9\n\nthe _n_th decimal of _N_ shall be:\n\n 1, 2, 3, 4, 5, 6, 7, 8, 1, 1\n\n [15] _Revue g\u00e9n\u00e9rale des sciences_, June 30, 1905.\n\nAs we see, _N_ is not equal to the _n_th number of _E_, and as _n_ is\narbitrary, _N_ does not appertain to _E_ and yet _N_ should belong to\nthis assemblage since we have defined it with a finite number of words.\n\nWe shall later see that M. Richard has himself given with much sagacity\nthe explanation of his paradox and that this extends, _mutatis\nmutandis_, to the other like paradoxes. Again, Russell cites another\nquite amusing paradox: _What is the least whole number which can not be\ndefined by a phrase composed of less than a hundred English words_?\n\nThis number exists; and in fact the numbers capable of being defined by\na like phrase are evidently finite in number since the words of the\nEnglish language are not infinite in number. Therefore among them will\nbe one less than all the others. And, on the other hand, this number\ndoes not exist, because its definition implies contradiction. This\nnumber, in fact, is defined by the phrase in italics which is composed\nof less than a hundred English words; and by definition this number\nshould not be capable of definition by a like phrase.\n\n\nVI\n\n_Zigzag Theory and No-class Theory_\n\nWhat is Mr. Russell's attitude in presence of these contradictions?\nAfter having analyzed those of which we have just spoken, and cited\nstill others, after having given them a form recalling Epimenides, he\ndoes not hesitate to conclude: \"A propositional function of one\nvariable does not always determine a class.\" A propositional function\n(that is to say a definition) does not always determine a class. A\n'propositional function' or 'norm' may be 'non-predicative.' And this\ndoes not mean that these non-predicative propositions determine an empty\nclass, a null class; this does not mean that there is no value of x\nsatisfying the definition and capable of being one of the elements of\nthe class. The elements exist, but they have no right to unite in a\nsyndicate to form a class.\n\nBut this is only the beginning and it is needful to know how to\nrecognize whether a definition is or is not predicative. To solve this\nproblem Russell hesitates between three theories which he calls\n\nA. The zigzag theory;\n\nB. The theory of limitation of size;\n\nC. The no-class theory.\n\nAccording to the zigzag theory \"definitions (propositional functions)\ndetermine a class when they are very simple and cease to do so only when\nthey are complicated and obscure.\" Who, now, is to decide whether a\ndefinition may be regarded as simple enough to be acceptable? To this\nquestion there is no answer, if it be not the loyal avowal of a complete\ninability: \"The rules which enable us to recognize whether these\ndefinitions are predicative would be extremely complicated and can not\ncommend themselves by any plausible reason. This is a fault which might\nbe remedied by greater ingenuity or by using distinctions not yet\npointed out. But hitherto in seeking these rules, I have not been able\nto find any other directing principle than the absence of\ncontradiction.\"\n\nThis theory therefore remains very obscure; in this night a single\nlight--the word zigzag. What Russell calls the 'zigzaginess' is\ndoubtless the particular characteristic which distinguishes the argument\nof Epimenides.\n\nAccording to the theory of limitation of size, a class would cease to\nhave the right to exist if it were too extended. Perhaps it might be\ninfinite, but it should not be too much so. But we always meet again the\nsame difficulty; at what precise moment does it begin to be too much\nso? Of course this difficulty is not solved and Russell passes on to the\nthird theory.\n\nIn the no-classes theory it is forbidden to speak the word 'class' and\nthis word must be replaced by various periphrases. What a change for\nlogistic which talks only of classes and classes of classes! It becomes\nnecessary to remake the whole of logistic. Imagine how a page of\nlogistic would look upon suppressing all the propositions where it is a\nquestion of class. There would only be some scattered survivors in the\nmidst of a blank page. _Apparent rari nantes in gurgite vasto._\n\nBe that as it may, we see how Russell hesitates and the modifications to\nwhich he submits the fundamental principles he has hitherto adopted.\nCriteria are needed to decide whether a definition is too complex or too\nextended, and these criteria can only be justified by an appeal to\nintuition.\n\nIt is toward the no-classes theory that Russell finally inclines. Be\nthat as it may, logistic is to be remade and it is not clear how much of\nit can be saved. Needless to add that Cantorism and logistic are alone\nunder consideration; real mathematics, that which is good for something,\nmay continue to develop in accordance with its own principles without\nbothering about the storms which rage outside it, and go on step by step\nwith its usual conquests which are final and which it never has to\nabandon.\n\n\nVII\n\n_The True Solution_\n\nWhat choice ought we to make among these different theories? It seems to\nme that the solution is contained in a letter of M. Richard of which I\nhave spoken above, to be found in the _Revue g\u00e9n\u00e9rale des sciences_ of\nJune 30, 1905. After having set forth the antinomy we have called\nRichard's antinomy, he gives its explanation. Recall what has already\nbeen said of this antinomy. _E_ is the aggregate of _all_ the numbers\ndefinable by a finite number of words, _without introducing the notion\nof the aggregate E itself_. Else the definition of _E_ would contain a\nvicious circle; we must not define _E_ by the aggregate _E_ itself.\n\nNow we have defined _N_ with a finite number of words, it is true, but\nwith the aid of the notion of the aggregate _E_. And this is why _N_ is\nnot part of _E_. In the example selected by M. Richard, the conclusion\npresents itself with complete evidence and the evidence will appear\nstill stronger on consulting the text of the letter itself. But the same\nexplanation holds good for the other antinomies, as is easily verified.\nThus _the definitions which should be regarded as not predicative are\nthose which contain a vicious circle_. And the preceding examples\nsufficiently show what I mean by that. Is it this which Russell calls\nthe 'zigzaginess'? I put the question without answering it.\n\n\nVIII\n\n_The Demonstrations of the Principle of Induction_\n\nLet us now examine the pretended demonstrations of the principle of\ninduction and in particular those of Whitehead and of Burali-Forti.\n\nWe shall speak of Whitehead's first, and take advantage of certain new\nterms happily introduced by Russell in his recent memoir. Call\n_recurrent class_ every class containing zero, and containing _n_ + 1 if\nit contains _n_. Call _inductive number_ every number which is a part of\n_all_ the recurrent classes. Upon what condition will this latter\ndefinition, which plays an essential r\u00f4le in Whitehead's proof, be\n'predicative' and consequently acceptable?\n\nIn accordance with what has been said, it is necessary to understand by\n_all_ the recurrent classes, all those in whose definition the notion of\ninductive number does not enter. Else we fall again upon the vicious\ncircle which has engendered the antinomies.\n\nNow _Whitehead has not taken this precaution_. Whitehead's reasoning is\ntherefore fallacious; it is the same which led to the antinomies. It was\nillegitimate when it gave false results; it remains illegitimate when by\nchance it leads to a true result.\n\nA definition containing a vicious circle defines nothing. It is of no\nuse to say, we are sure, whatever meaning we may give to our definition,\nzero at least belongs to the class of inductive numbers; it is not a\nquestion of knowing whether this class is void, but whether it can be\nrigorously deliminated. A 'non-predicative' class is not an empty\nclass, it is a class whose boundary is undetermined. Needless to add\nthat this particular objection leaves in force the general objections\napplicable to all the demonstrations.\n\n\nIX\n\nBurali-Forti has given another demonstration.[16] But he is obliged to\nassume two postulates: First, there always exists at least one infinite\nclass. The second is thus expressed:\n\n u[epsilon]K(K - [iota][Lambda]) \u00b7 [inverted c] \u00b7 u < v'u.\n\nThe first postulate is not more evident than the principle to be proved.\nThe second not only is not evident, but it is false, as Whitehead has\nshown; as moreover any recruit would see at the first glance, if the\naxiom had been stated in intelligible language, since it means that the\nnumber of combinations which can be formed with several objects is less\nthan the number of these objects.\n\n [16] In his article 'Le classi finite,' _Atti di Torino_, Vol. XXXII.\n\n\nX\n\n_Zermelo's Assumption_\n\nA famous demonstration by Zermelo rests upon the following assumption:\nIn any aggregate (or the same in each aggregate of an assemblage of\naggregates) we can always choose _at random_ an element (even if this\nassemblage of aggregates should contain an infinity of aggregates). This\nassumption had been applied a thousand times without being stated, but,\nonce stated, it aroused doubts. Some mathematicians, for instance\nM. Borel, resolutely reject it; others admire it. Let us see what,\naccording to his last article, Russell thinks of it. He does not speak\nout, but his reflections are very suggestive.\n\nAnd first a picturesque example: Suppose we have as many pairs of shoes\nas there are whole numbers, and so that we can number _the pairs_ from\none to infinity, how many shoes shall we have? Will the number of shoes\nbe equal to the number of pairs? Yes, if in each pair the right shoe is\ndistinguishable from the left; it will in fact suffice to give the\nnumber 2_n_ - 1 to the right shoe of the _n_th pair, and the number 2_n_\nto the left shoe of the _n_th pair. No, if the right shoe is just like\nthe left, because a similar operation would become impossible--unless we\nadmit Zermelo's assumption, since then we could choose _at random_ in\neach pair the shoe to be regarded as the right.\n\n\nXI\n\n_Conclusions_\n\nA demonstration truly founded upon the principles of analytic logic will\nbe composed of a series of propositions. Some, serving as premises, will\nbe identities or definitions; the others will be deduced from the\npremises step by step. But though the bond between each proposition and\nthe following is immediately evident, it will not at first sight appear\nhow we get from the first to the last, which we may be tempted to regard\nas a new truth. But if we replace successively the different expressions\ntherein by their definition and if this operation be carried as far as\npossible, there will finally remain only identities, so that all will\nreduce to an immense tautology. Logic therefore remains sterile unless\nmade fruitful by intuition.\n\nThis I wrote long ago; logistic professes the contrary and thinks it has\nproved it by actually proving new truths. By what mechanism? Why in\napplying to their reasonings the procedure just described--namely,\nreplacing the terms defined by their definitions--do we not see them\ndissolve into identities like ordinary reasonings? It is because this\nprocedure is not applicable to them. And why? Because their definitions\nare not predicative and present this sort of hidden vicious circle which\nI have pointed out above; non-predicative definitions can not be\nsubstituted for the terms defined. Under these conditions _logistic is\nnot sterile, it engenders antinomies_.\n\nIt is the belief in the existence of the actual infinite which has given\nbirth to those non-predicative definitions. Let me explain. In these\ndefinitions the word 'all' figures, as is seen in the examples cited\nabove. The word 'all' has a very precise meaning when it is a question\nof a finite number of objects; to have another one, when the objects are\ninfinite in number, would require there being an actual (given complete)\ninfinity. Otherwise _all_ these objects could not be conceived as\npostulated anteriorly to their definition, and then if the definition of\na notion _N_ depends upon _all_ the objects _A_, it may be infected with\na vicious circle, if among the objects _A_ are some indefinable without\nthe intervention of the notion _N_ itself.\n\nThe rules of formal logic express simply the properties of all possible\nclassifications. But for them to be applicable it is necessary that\nthese classifications be immutable and that we have no need to modify\nthem in the course of the reasoning. If we have to classify only a\nfinite number of objects, it is easy to keep our classifications without\nchange. If the objects are _indefinite_ in number, that is to say if one\nis constantly exposed to seeing new and unforeseen objects arise, it may\nhappen that the appearance of a new object may require the\nclassification to be modified, and thus it is we are exposed to\nantinomies. _There is no actual (given complete) infinity._ The\nCantorians have forgotten this, and they have fallen into contradiction.\nIt is true that Cantorism has been of service, but this was when applied\nto a real problem whose terms were precisely defined, and then we could\nadvance without fear.\n\nLogistic also forgot it, like the Cantorians, and encountered the same\ndifficulties. But the question is to know whether they went this way by\naccident or whether it was a necessity for them. For me, the question is\nnot doubtful; belief in an actual infinity is essential in the Russell\nlogic. It is just this which distinguishes it from the Hilbert logic.\nHilbert takes the view-point of extension, precisely in order to avoid\nthe Cantorian antinomies. Russell takes the view-point of comprehension.\nConsequently for him the genus is anterior to the species, and the\n_summum genus_ is anterior to all. That would not be inconvenient if the\n_summum genus_ was finite; but if it is infinite, it is necessary to\npostulate the infinite, that is to say to regard the infinite as actual\n(given complete). And we have not only infinite classes; when we pass\nfrom the genus to the species in restricting the concept by new\nconditions, these conditions are still infinite in number. Because they\nexpress generally that the envisaged object presents such or such a\nrelation with all the objects of an infinite class.\n\nBut that is ancient history. Russell has perceived the peril and takes\ncounsel. He is about to change everything, and, what is easily\nunderstood, he is preparing not only to introduce new principles which\nshall allow of operations formerly forbidden, but he is preparing to\nforbid operations he formerly thought legitimate. Not content to adore\nwhat he burned, he is about to burn what he adored, which is more\nserious. He does not add a new wing to the building, he saps its\nfoundation.\n\nThe old logistic is dead, so much so that already the zigzag theory and\nthe no-classes theory are disputing over the succession. To judge of the\nnew, we shall await its coming.\n\n\n\n\nBOOK III\n\n\nTHE NEW MECHANICS\n\n\n\n\nCHAPTER I\n\nMECHANICS AND RADIUM\n\n\nI\n\n_Introduction_\n\nThe general principles of Dynamics, which have, since Newton, served as\nfoundation for physical science, and which appeared immovable, are they\non the point of being abandoned or at least profoundly modified? This is\nwhat many people have been asking themselves for some years. According\nto them, the discovery of radium has overturned the scientific dogmas we\nbelieved the most solid: on the one hand, the impossibility of the\ntransmutation of metals; on the other hand, the fundamental postulates\nof mechanics.\n\nPerhaps one is too hasty in considering these novelties as finally\nestablished, and breaking our idols of yesterday; perhaps it would be\nproper, before taking sides, to await experiments more numerous and more\nconvincing. None the less is it necessary, from to-day, to know the new\ndoctrines and the arguments, already very weighty, upon which they rest.\n\nIn few words let us first recall in what those principles consist:\n\n_A._ The motion of a material point isolated and apart from all exterior\nforce is straight and uniform; this is the principle of inertia: without\nforce no acceleration;\n\n_B._ The acceleration of a moving point has the same direction as the\nresultant of all the forces to which it is subjected; it is equal to the\nquotient of this resultant by a coefficient called _mass_ of the moving\npoint.\n\nThe mass of a moving point, so defined, is a constant; it does not\ndepend upon the velocity acquired by this point; it is the same whether\nthe force, being parallel to this velocity, tends only to accelerate or\nto retard the motion of the point, or whether, on the contrary, being\nperpendicular to this velocity, it tends to make this motion deviate\ntoward the right, or the left, that is to say to _curve_ the trajectory;\n\n_C._ All the forces affecting a material point come from the action of\nother material points; they depend only upon the _relative_ positions\nand velocities of these different material points.\n\nCombining the two principles _B_ and _C_, we reach the _principle of\nrelative motion_, in virtue of which the laws of the motion of a system\nare the same whether we refer this system to fixed axes, or to moving\naxes animated by a straight and uniform motion of translation, so that\nit is impossible to distinguish absolute motion from a relative motion\nwith reference to such moving axes;\n\n_D._ If a material point _A_ acts upon another material point _B_, the\nbody _B_ reacts upon _A_, and these two actions are two equal and\ndirectly opposite forces. This is _the principle of the equality of\naction and reaction_, or, more briefly, the _principle of reaction_.\n\nAstronomic observations and the most ordinary physical phenomena seem to\nhave given of these principles a confirmation complete, constant and\nvery precise. This is true, it is now said, but it is because we have\nnever operated with any but very small velocities; Mercury, for example,\nthe fastest of the planets, goes scarcely 100 kilometers a second. Would\nthis planet act the same if it went a thousand times faster? We see\nthere is yet no need to worry; whatever may be the progress of\nautomobilism, it will be long before we must give up applying to our\nmachines the classic principles of dynamics.\n\nHow then have we come to make actual speeds a thousand times greater\nthan that of Mercury, equal, for instance, to a tenth or a third of the\nvelocity of light, or approaching still more closely to that velocity?\nIt is by aid of the cathode rays and the rays from radium.\n\nWe know that radium emits three kinds of rays, designated by the three\nGreek letters [alpha], [beta], [gamma]; in what follows, unless the\ncontrary be expressly stated, it will always be a question of the [beta]\nrays, which are analogous to the cathode rays.\n\nAfter the discovery of the cathode rays two theories appeared. Crookes\nattributed the phenomena to a veritable molecular bombardment; Hertz, to\nspecial undulations of the ether. This was a renewal of the debate which\ndivided physicists a century ago about light; Crookes took up the\nemission theory, abandoned for light; Hertz held to the undulatory\ntheory. The facts seem to decide in favor of Crookes.\n\nIt has been recognized, in the first place, that the cathode rays carry\nwith them a negative electric charge; they are deviated by a magnetic\nfield and by an electric field; and these deviations are precisely such\nas these same fields would produce upon projectiles animated by a very\nhigh velocity and strongly charged with electricity. These two\ndeviations depend upon two quantities: one the velocity, the other the\nrelation of the electric charge of the projectile to its mass; we cannot\nknow the absolute value of this mass, nor that of the charge, but only\ntheir relation; in fact, it is clear that if we double at the same time\nthe charge and the mass, without changing the velocity, we shall double\nthe force which tends to deviate the projectile, but, as its mass is\nalso doubled, the acceleration and deviation observable will not be\nchanged. The observation of the two deviations will give us therefore\ntwo equations to determine these two unknowns. We find a velocity of\nfrom 10,000 to 30,000 kilometers a second; as to the ratio of the charge\nto the mass, it is very great. We may compare it to the corresponding\nratio in regard to the hydrogen ion in electrolysis; we then find that a\ncathodic projectile carries about a thousand times more electricity than\nan equal mass of hydrogen would carry in an electrolyte.\n\nTo confirm these views, we need a direct measurement of this velocity to\ncompare with the velocity so calculated. Old experiments of J. J.\nThomson had given results more than a hundred times too small; but they\nwere exposed to certain causes of error. The question was taken up again\nby Wiechert in an arrangement where the Hertzian oscillations were\nutilized; results were found agreeing with the theory, at least as to\norder of magnitude; it would be of great interest to repeat these\nexperiments. However that may be, the theory of undulations appears\npowerless to account for this complex of facts.\n\nThe same calculations made with reference to the [beta] rays of radium\nhave given velocities still greater: 100,000 or 200,000 kilometers or\nmore yet. These velocities greatly surpass all those we know. It is true\nthat light has long been known to go 300,000 kilometers a second; but it\nis not a carrying of matter, while, if we adopt the emission theory for\nthe cathode rays, there would be material molecules really impelled at\nthe velocities in question, and it is proper to investigate whether the\nordinary laws of mechanics are still applicable to them.\n\n\nII\n\n_Mass Longitudinal and Mass Transversal_\n\nWe know that electric currents produce the phenomena of induction, in\nparticular _self-induction_. When a current increases, there develops an\nelectromotive force of self-induction which tends to oppose the current;\non the contrary, when the current decreases, the electromotive force of\nself-induction tends to maintain the current. The self-induction\ntherefore opposes every variation of the intensity of the current, just\nas in mechanics the inertia of a body opposes every variation of its\nvelocity.\n\n_Self-induction is a veritable inertia._ Everything happens as if the\ncurrent could not establish itself without putting in motion the\nsurrounding ether and as if the inertia of this ether tended, in\nconsequence, to keep constant the intensity of this current. It would be\nrequisite to overcome this inertia to establish the current, it would be\nnecessary to overcome it again to make the current cease.\n\nA cathode ray, which is a rain of projectiles charged with negative\nelectricity, may be likened to a current; doubtless this current\ndiffers, at first sight at least, from the currents of ordinary\nconduction, where the matter does not move and where the electricity\ncirculates through the matter. This is a _current of convection_, where\nthe electricity, attached to a material vehicle, is carried along by the\nmotion of this vehicle. But Rowland has proved that currents of\nconvection produce the same magnetic effects as currents of conduction;\nthey should produce also the same effects of induction. First, if this\nwere not so, the principle of the conservation of energy would be\nviolated; besides, Cr\u00e9mieu and Pender have employed a method putting in\nevidence _directly_ these effects of induction.\n\nIf the velocity of a cathode corpuscle varies, the intensity of the\ncorresponding current will likewise vary; and there will develop effects\nof self-induction which will tend to oppose this variation. These\ncorpuscles should therefore possess a double inertia: first their own\nproper inertia, and then the apparent inertia, due to self-induction,\nwhich produces the same effects. They will therefore have a total\napparent mass, composed of their real mass and of a fictitious mass of\nelectromagnetic origin. Calculation shows that this fictitious mass\nvaries with the velocity, and that the force of inertia of\nself-induction is not the same when the velocity of the projectile\naccelerates or slackens, or when it is deviated; therefore so it is with\nthe force of the total apparent inertia.\n\nThe total apparent mass is therefore not the same when the real force\napplied to the corpuscle is parallel to its velocity and tends to\naccelerate the motion as when it is perpendicular to this velocity and\ntends to make the direction vary. It is necessary therefore to\ndistinguish the _total longitudinal mass_ from the _total transversal\nmass_. These two total masses depend, moreover, upon the velocity. This\nfollows from the theoretical work of Abraham.\n\nIn the measurements of which we speak in the preceding section, what is\nit we determine in measuring the two deviations? It is the velocity on\nthe one hand, and on the other hand the ratio of the charge to the\n_total transversal mass_. How, under these conditions, can we make out\nin this total mass the part of the real mass and that of the fictitious\nelectromagnetic mass? If we had only the cathode rays properly so\ncalled, it could not be dreamed of; but happily we have the rays of\nradium which, as we have seen, are notably swifter. These rays are not\nall identical and do not behave in the same way under the action of an\nelectric field and a magnetic field. It is found that the electric\ndeviation is a function of the magnetic deviation, and we are able, by\nreceiving on a sensitive plate radium rays which have been subjected to\nthe action of the two fields, to photograph the curve which represents\nthe relation between these two deviations. This is what Kaufmann has\ndone, deducing from it the relation between the velocity and the ratio\nof the charge to the total apparent mass, a ratio we shall call\n[epsilon].\n\nOne might suppose there are several species of rays, each characterized\nby a fixed velocity, by a fixed charge and by a fixed mass. But this\nhypothesis is improbable; why, in fact, would all the corpuscles of the\nsame mass take always the same velocity? It is more natural to suppose\nthat the charge as well as the _real_ mass are the same for all the\nprojectiles, and that these differ only by their velocity. If the ratio\n[epsilon] is a function of the velocity, this is not because the real\nmass varies with this velocity; but, since the fictitious\nelectromagnetic mass depends upon this velocity, the total apparent\nmass, alone observable, must depend upon it, though the real mass does\nnot depend upon it and may be constant.\n\nThe calculations of Abraham let us know the law according to which the\n_fictitious_ mass varies as a function of the velocity; Kaufmann's\nexperiment lets us know the law of variation of the _total_ mass.\n\nThe comparison of these two laws will enable us therefore to determine\nthe ratio of the real mass to the total mass.\n\nSuch is the method Kaufmann used to determine this ratio. The result is\nhighly surprising: _the real mass is naught_.\n\nThis has led to conceptions wholly unexpected. What had only been proved\nfor cathode corpuscles was extended to all bodies. What we call mass\nwould be only semblance; all inertia would be of electromagnetic origin.\nBut then mass would no longer be constant, it would augment with the\nvelocity; sensibly constant for velocities up to 1,000 kilometers a\nsecond, it then would increase and would become infinite for the\nvelocity of light. The transversal mass would no longer be equal to the\nlongitudinal: they would only be nearly equal if the velocity is not too\ngreat. The principle _B_ of mechanics would no longer be true.\n\n\nIII\n\n_The Canal Rays_\n\nAt the point where we now are, this conclusion might seem premature. Can\none apply to all matter what has been proved only for such light\ncorpuscles, which are a mere emanation of matter and perhaps not true\nmatter? But before entering upon this question, a word must be said of\nanother sort of rays. I refer to the _canal rays_, the _Kanalstrahlen_\nof Goldstein.\n\nThe cathode, together with the cathode rays charged with negative\nelectricity, emits canal rays charged with positive electricity. In\ngeneral, these canal rays not being repelled by the cathode, are\nconfined to the immediate neighborhood of this cathode, where they\nconstitute the `chamois cushion,' not very easy to perceive; but, if the\ncathode is pierced with holes and if it almost completely blocks up the\ntube, the canal rays spread _back_ of the cathode, in the direction\nopposite to that of the cathode rays, and it becomes possible to study\nthem. It is thus that it has been possible to show their positive charge\nand to show that the magnetic and electric deviations still exist, as\nfor the cathode rays, but are much feebler.\n\nRadium likewise emits rays analogous to the canal rays, and relatively\nvery absorbable, called [alpha] rays.\n\nWe can, as for the cathode rays, measure the two deviations and thence\ndeduce the velocity and the ratio [epsilon]. The results are less\nconstant than for the cathode rays, but the velocity is less, as well as\nthe ratio [epsilon]; the positive corpuscles are less charged than the\nnegative; or if, which is more natural, we suppose the charges equal and\nof opposite sign, the positive corpuscles are much the larger. These\ncorpuscles, charged the ones positively, the others negatively, have\nbeen called _electrons_.\n\n\nIV\n\n_The Theory of Lorentz_\n\nBut the electrons do not merely show us their existence in these rays\nwhere they are endowed with enormous velocities. We shall see them in\nvery different r\u00f4les, and it is they that account for the principal\nphenomena of optics and electricity. The brilliant synthesis about to be\nnoticed is due to Lorentz.\n\nMatter is formed solely of electrons carrying enormous charges, and, if\nit seems to us neutral, this is because the charges of opposite sign of\nthese electrons compensate each other. We may imagine, for example, a\nsort of solar system formed of a great positive electron, around which\ngravitate numerous little planets, the negative electrons, attracted by\nthe electricity of opposite name which charges the central electron. The\nnegative charges of these planets would balance the positive charge of\nthis sun, so that the algebraic sum of all these charges would be\nnaught.\n\nAll these electrons swim in the ether. The ether is everywhere\nidentically the same, and perturbations in it are propagated according\nto the same laws as light or the Hertzian oscillations _in vacuo_. There\nis nothing but electrons and ether. When a luminous wave enters a part\nof the ether where electrons are numerous, these electrons are put in\nmotion under the influence of the perturbation of the ether, and they\nthen react upon the ether. So would be explained refraction, dispersion,\ndouble refraction and absorption. Just so, if for any cause an electron\nbe put in motion, it would trouble the ether around it and would give\nrise to luminous waves, and this would explain the emission of light by\nincandescent bodies.\n\nIn certain bodies, the metals for example, we should have fixed\nelectrons, between which would circulate moving electrons enjoying\nperfect liberty, save that of going out from the metallic body and\nbreaking the surface which separates it from the exterior void or from\nthe air, or from any other non-metallic body.\n\nThese movable electrons behave then, within the metallic body, as do,\naccording to the kinetic theory of gases, the molecules of a gas within\nthe vase where this gas is confined. But, under the influence of a\ndifference of potential, the negative movable electrons would tend to go\nall to one side, and the positive movable electrons to the other. This\nis what would produce electric currents, and _this is why these bodies\nwould be conductors_. On the other hand, the velocities of our electrons\nwould be the greater the higher the temperature, if we accept the\nassimilation with the kinetic theory of gases. When one of these movable\nelectrons encounters the surface of the metallic body, whose boundary it\ncan not pass, it is reflected like a billiard ball which has hit the\ncushion, and its velocity undergoes a sudden change of direction. But\nwhen an electron changes direction, as we shall see further on, it\nbecomes the source of a luminous wave, and this is why hot metals are\nincandescent.\n\nIn other bodies, the dielectrics and the transparent bodies, the movable\nelectrons enjoy much less freedom. They remain as if attached to fixed\nelectrons which attract them. The farther they go away from them the\ngreater becomes this attraction and tends to pull them back. They\ntherefore can make only small excursions; they can no longer circulate,\nbut only oscillate about their mean position. This is why these bodies\nwould not be conductors; moreover they would most often be transparent,\nand they would be refractive, since the luminous vibrations would be\ncommunicated to the movable electrons, susceptible of oscillation, and\nthence a perturbation would result.\n\nI can not here give the details of the calculations; I confine myself to\nsaying that this theory accounts for all the known facts, and has\npredicted new ones, such as the Zeeman effect.\n\n\nV\n\n_Mechanical Consequences_\n\nWe now may face two hypotheses:\n\n1\u00ba The positive electrons have a real mass, much greater than their\nfictitious electromagnetic mass; the negative electrons alone lack real\nmass. We might even suppose that apart from electrons of the two signs,\nthere are neutral atoms which have only their real mass. In this case,\nmechanics is not affected; there is no need of touching its laws; the\nreal mass is constant; simply, motions are deranged by the effects of\nself-induction, as has always been known; moreover, these perturbations\nare almost negligible, except for the negative electrons which, not\nhaving real mass, are not true matter.\n\n2\u00ba But there is another point of view; we may suppose there are no\nneutral atoms, and the positive electrons lack real mass just as the\nnegative electrons. But then, real mass vanishing, either the word\n_mass_ will no longer have any meaning, or else it must designate the\nfictitious electromagnetic mass; in this case, mass will no longer be\nconstant, the transversal _mass_ will no longer be equal to the\nlongitudinal, the principles of mechanics will be overthrown.\n\nFirst a word of explanation. We have said that, for the same charge, the\n_total_ mass of a positive electron is much greater than that of a\nnegative. And then it is natural to think that this difference is\nexplained by the positive electron having, besides its fictitious mass,\na considerable real mass; which takes us back to the first hypothesis.\nBut we may just as well suppose that the real mass is null for these as\nfor the others, but that the fictitious mass of the positive electron is\nmuch the greater since this electron is much the smaller. I say\nadvisedly: much the smaller. And, in fact, in this hypothesis inertia is\nexclusively electromagnetic in origin; it reduces itself to the inertia\nof the ether; the electrons are no longer anything by themselves; they\nare solely holes in the ether and around which the ether moves; the\nsmaller these holes are, the more will there be of ether, the greater,\nconsequently, will be the inertia of the ether.\n\nHow shall we decide between these two hypotheses? By operating upon the\ncanal rays as Kaufmann did upon the [beta] rays? This is impossible; the\nvelocity of these rays is much too slight. Should each therefore decide\naccording to his temperament, the conservatives going to one side and\nthe lovers of the new to the other? Perhaps, but, to fully understand\nthe arguments of the innovators, other considerations must come in.\n\n\n\n\nCHAPTER II\n\nMECHANICS AND OPTICS\n\n\nI\n\n_Aberration_\n\nYou know in what the phenomenon of aberration, discovered by Bradley,\nconsists. The light issuing from a star takes a certain time to go\nthrough a telescope; during this time, the telescope, carried along by\nthe motion of the earth, is displaced. If therefore the telescope were\npointed in the _true_ direction of the star, the image would be formed\nat the point occupied by the crossing of the threads of the network when\nthe light has reached the objective; and this crossing would no longer\nbe at this same point when the light reached the plane of the network.\nWe would therefore be led to mis-point the telescope to bring the image\nupon the crossing of the threads. Thence results that the astronomer\nwill not point the telescope in the direction of the absolute velocity\nof the light, that is to say toward the true position of the star, but\njust in the direction of the relative velocity of the light with\nreference to the earth, that is to say toward what is called the\napparent position of the star.\n\nThe velocity of light is known; we might therefore suppose that we have\nthe means of calculating the _absolute_ velocity of the earth. (I shall\nsoon explain my use here of the word absolute.) Nothing of the sort; we\nindeed know the apparent position of the star we observe; but we do not\nknow its true position; we know the velocity of the light only in\nmagnitude and not in direction.\n\nIf therefore the absolute velocity of the earth were straight and\nuniform, we should never have suspected the phenomenon of aberration;\nbut it is variable; it is composed of two parts: the velocity of the\nsolar system, which is straight and uniform; the velocity of the earth\nwith reference to the sun, which is variable. If the velocity of the\nsolar system, that is to say if the constant part existed alone, the\nobserved direction would be invariable. This position that one would\nthus observe is called the _mean_ apparent position of the star.\n\nTaking account now at the same time of the two parts of the velocity of\nthe earth, we shall have the actual apparent position, which describes a\nlittle ellipse around the mean apparent position, and it is this ellipse\nthat we observe.\n\nNeglecting very small quantities, we shall see that the dimensions of\nthis ellipse depend only upon the ratio of the velocity of the earth\nwith reference to the sun to the velocity of light, so that the relative\nvelocity of the earth with regard to the sun has alone come in.\n\nBut wait! This result is not exact, it is only approximate; let us push\nthe approximation a little farther. The dimensions of the ellipse will\ndepend then upon the absolute velocity of the earth. Let us compare the\nmajor axes of the ellipse for the different stars: we shall have,\ntheoretically at least, the means of determining this absolute velocity.\n\nThat would be perhaps less shocking than it at first seems; it is a\nquestion, in fact, not of the velocity with reference to an absolute\nvoid, but of the velocity with regard to the ether, which is taken _by\ndefinition_ as being absolutely at rest.\n\nBesides, this method is purely theoretical. In fact, the aberration is\nvery small; the possible variations of the ellipse of aberration are\nmuch smaller yet, and, if we consider the aberration as of the first\norder, they should therefore be regarded as of the second order: about a\nmillionth of a second; they are absolutely inappreciable for our\ninstruments. We shall finally see, further on, why the preceding theory\nshould be rejected, and why we could not determine this absolute\nvelocity even if our instruments were ten thousand times more precise!\n\nOne might imagine some other means, and in fact, so one has. The\nvelocity of light is not the same in water as in air; could we not\ncompare the two apparent positions of a star seen through a telescope\nfirst full of air, then full of water? The results have been negative;\nthe apparent laws of reflection and refraction are not altered by the\nmotion of the earth. This phenomenon is capable of two explanations:\n\n1\u00ba It might be supposed that the ether is not at rest, but that it is\ncarried along by the body in motion. It would then not be astonishing\nthat the phenomena of refraction are not altered by the motion of the\nearth, since all, prisms, telescopes and ether, are carried along\ntogether in the same translation. As to the aberration itself, it would\nbe explained by a sort of refraction happening at the surface of\nseparation of the ether at rest in the interstellar spaces and the ether\ncarried along by the motion of the earth. It is upon this hypothesis\n(bodily carrying along of the ether) that is founded the _theory of\nHertz_ on the electrodynamics of moving bodies.\n\n2\u00ba Fresnel, on the contrary, supposes that the ether is at absolute rest\nin the void, at rest almost absolute in the air, whatever be the\nvelocity of this air, and that it is partially carried along by\nrefractive media. Lorentz has given to this theory a more satisfactory\nform. For him, the ether is at rest, only the electrons are in motion;\nin the void, where it is only a question of the ether, in the air, where\nthis is almost the case, the carrying along is null or almost null; in\nrefractive media, where perturbation is produced at the same time by\nvibrations of the ether and those of electrons put in swing by the\nagitation of the ether, the undulations are _partially_ carried along.\n\nTo decide between the two hypotheses, we have Fizeau's experiment,\ncomparing by measurements of the fringes of interference, the velocity\nof light in air at rest or in motion. These experiments have confirmed\nFresnel's hypothesis of partial carrying along. They have been repeated\nwith the same result by Michelson. _The theory of Hertz must therefore\nbe rejected._\n\n\nII\n\n_The Principle of Relativity_\n\nBut if the ether is not carried along by the motion of the earth, is it\npossible to show, by means of optical phenomena, the absolute velocity\nof the earth, or rather its velocity with respect to the unmoving ether?\nExperiment has answered negatively, and yet the experimental procedures\nhave been varied in all possible ways. Whatever be the means employed\nthere will never be disclosed anything but relative velocities; I mean\nthe velocities of certain material bodies with reference to other\nmaterial bodies. In fact, if the source of light and the apparatus of\nobservation are on the earth and participate in its motion, the\nexperimental results have always been the same, whatever be the\norientation of the apparatus with reference to the orbital motion of the\nearth. If astronomic aberration happens, it is because the source, a\nstar, is in motion with reference to the observer.\n\nThe hypotheses so far made perfectly account for this general result,\n_if we neglect very small quantities of the order of the square of the\naberration_. The explanation rests upon the notion of _local time_,\nintroduced by Lorentz, which I shall try to make clear. Suppose two\nobservers, placed one at _A_, the other at _B_, and wishing to set their\nwatches by means of optical signals. They agree that _B_ shall send a\nsignal to _A_ when his watch marks an hour determined upon, and _A_ is\nto put his watch to that hour the moment he sees the signal. If this\nalone were done, there would be a systematic error, because as the light\ntakes a certain time _t_ to go from _B_ to _A_, _A_'s watch would be\nbehind _B_'s the time _t_. This error is easily corrected. It suffices\nto cross the signals. _A_ in turn must signal _B_, and, after this new\nadjustment, _B_'s watch will be behind _A_'s the time _t_. Then it will\nbe sufficient to take the arithmetic mean of the two adjustments.\n\nBut this way of doing supposes that light takes the same time to go from\n_A_ to _B_ as to return from _B_ to _A_. That is true if the observers\nare motionless; it is no longer so if they are carried along in a common\ntranslation, since then _A_, for example, will go to meet the light\ncoming from _B_, while _B_ will flee before the light coming from _A_.\nIf therefore the observers are borne along in a common translation and\nif they do not suspect it, their adjustment will be defective; their\nwatches will not indicate the same time; each will show the _local time_\nbelonging to the point where it is.\n\nThe two observers will have no way of perceiving this, if the unmoving\nether can transmit to them only luminous signals all of the same\nvelocity, and if the other signals they might send are transmitted by\nmedia carried along with them in their translation. The phenomenon each\nobserves will be too soon or too late; it would be seen at the same\ninstant only if the translation did not exist; but as it will be\nobserved with a watch that is wrong, this will not be perceived and the\nappearances will not be altered.\n\nIt results from this that the compensation is easy to explain so long as\nwe neglect the square of the aberration, and for a long time the\nexperiments were not sufficiently precise to warrant taking account of\nit. But the day came when Michelson imagined a much more delicate\nprocedure: he made rays interfere which had traversed different courses,\nafter being reflected by mirrors; each of the paths approximating a\nmeter and the fringes of interference permitting the recognition of a\nfraction of a thousandth of a millimeter, the square of the aberration\ncould no longer be neglected, and _yet the results were still negative_.\nTherefore the theory required to be completed, and it has been by the\n_Lorentz-Fitzgerald hypothesis_.\n\nThese two physicists suppose that all bodies carried along in a\ntranslation undergo a contraction in the sense of this translation,\nwhile their dimensions perpendicular to this translation remain\nunchanged. _This contraction is the same for all bodies_; moreover, it\nis very slight, about one two-hundred-millionth for a velocity such as\nthat of the earth. Furthermore our measuring instruments could not\ndisclose it, even if they were much more precise; our measuring rods in\nfact undergo the same contraction as the objects to be measured. If the\nmeter exactly fits when applied to a body, if we point the body and\nconsequently the meter in the sense of the motion of the earth, it will\nnot cease to exactly fit in another orientation, and that although the\nbody and the meter have changed in length as well as orientation, and\nprecisely because the change is the same for one as for the other. But\nit is quite different if we measure a length, not now with a meter, but\nby the time taken by light to pass along it, and this is just what\nMichelson has done.\n\nA body, spherical when at rest, will take thus the form of a flattened\nellipsoid of revolution when in motion; but the observer will always\nthink it spherical, since he himself has undergone an analogous\ndeformation, as also all the objects serving as points of reference. On\nthe contrary, the surfaces of the waves of light, remaining rigorously\nspherical, will seem to him elongated ellipsoids.\n\nWhat happens then? Suppose an observer and a source of light carried\nalong together in the translation: the wave surfaces emanating from the\nsource will be spheres having as centers the successive positions of the\nsource; the distance from this center to the actual position of the\nsource will be proportional to the time elapsed after the emission, that\nis to say to the radius of the sphere. All these spheres are therefore\nhomothetic one to the other, with relation to the actual position _S_ of\nthe source. But, for our observer, because of the contraction, all these\nspheres will seem elongated ellipsoids, and all these ellipsoids will\nmoreover be homothetic, with reference to the point _S_; the\nexcentricity of all these ellipsoids is the same and depends solely upon\nthe velocity of the earth. _We shall so select the law of contraction\nthat the point S may be at the focus of the meridian section of the\nellipsoid._\n\nThis time the compensation is _rigorous_, and this it is which explains\nMichelson's experiment.\n\nI have said above that, according to the ordinary theories, observations\nof the astronomic aberration would give us the absolute velocity of the\nearth, if our instruments were a thousand times more precise. I must\nmodify this statement. Yes, the observed angles would be modified by the\neffect of this absolute velocity, but the graduated circles we use to\nmeasure the angles would be deformed by the translation: they would\nbecome ellipses; thence would result an error in regard to the angle\nmeasured, and _this second error would exactly compensate the first_.\n\nThis Lorentz-Fitzgerald hypothesis seems at first very extraordinary;\nall we can say for the moment, in its favor, is that it is only the\nimmediate translation of Michelson's experimental result, if we _define_\nlengths by the time taken by light to run along them.\n\nHowever that may be, it is impossible to escape the impression that the\nprinciple of relativity is a general law of nature, that one will never\nbe able by any imaginable means to show any but relative velocities, and\nI mean by that not only the velocities of bodies with reference to the\nether, but the velocities of bodies with regard to one another. Too many\ndifferent experiments have given concordant results for us not to feel\ntempted to attribute to this principle of relativity a value comparable\nto that, for example, of the principle of equivalence. In any case, it\nis proper to see to what consequences this way of looking at things\nwould lead us and then to submit these consequences to the control of\nexperiment.\n\n\nIII\n\n_The Principle of Reaction_\n\nLet us see what the principle of the equality of action and reaction\nbecomes in the theory of Lorentz. Consider an electron _A_ which for any\ncause begins to move; it produces a perturbation in the ether; at the\nend of a certain time, this perturbation reaches another electron _B_,\nwhich will be disturbed from its position of equilibrium. In these\nconditions there can not be equality between action and reaction, at\nleast if we do not consider the ether, but only the electrons, _which\nalone are observable_, since our matter is made of electrons.\n\nIn fact it is the electron _A_ which has disturbed the electron _B_;\neven in case the electron _B_ should react upon _A_, this reaction could\nbe equal to the action, but in no case simultaneous, since the electron\n_B_ can begin to move only after a certain time, necessary for the\npropagation. Submitting the problem to a more exact calculation, we\nreach the following result: Suppose a Hertz discharger placed at the\nfocus of a parabolic mirror to which it is mechanically attached; this\ndischarger emits electromagnetic waves, and the mirror reflects all\nthese waves in the same direction; the discharger therefore will radiate\nenergy in a determinate direction. Well, the calculation shows that _the\ndischarger recoils_ like a cannon which has shot out a projectile. In\nthe case of the cannon, the recoil is the natural result of the equality\nof action and reaction. The cannon recoils because the projectile upon\nwhich it has acted reacts upon it. But here it is no longer the same.\nWhat has been sent out is no longer a material projectile: it is energy,\nand energy has no mass: it has no counterpart. And, in place of a\ndischarger, we could have considered just simply a lamp with a reflector\nconcentrating its rays in a single direction.\n\nIt is true that, if the energy sent out from the discharger or from the\nlamp meets a material object, this object receives a mechanical push as\nif it had been hit by a real projectile, and this push will be equal to\nthe recoil of the discharger and of the lamp, if no energy has been lost\non the way and if the object absorbs the whole of the energy. Therefore\none is tempted to say that there still is compensation between the\naction and the reaction. But this compensation, even should it be\ncomplete, is always belated. It never happens if the light, after\nleaving its source, wanders through interstellar spaces without ever\nmeeting a material body; it is incomplete, if the body it strikes is not\nperfectly absorbent.\n\nAre these mechanical actions too small to be measured, or are they\naccessible to experiment? These actions are nothing other than those due\nto the _Maxwell-Bartholi_ pressures; Maxwell had predicted these\npressures from calculations relative to electrostatics and magnetism;\nBartholi reached the same result by thermodynamic considerations.\n\nThis is how the _tails of comets_ are explained. Little particles detach\nthemselves from the nucleus of the comet; they are struck by the light\nof the sun, which pushes them back as would a rain of projectiles coming\nfrom the sun. The mass of these particles is so little that this\nrepulsion sweeps it away against the Newtonian attraction; so in moving\naway from the sun they form the tails.\n\nThe direct experimental verification was not easy to obtain. The first\nendeavor led to the construction of the _radiometer_. But this\ninstrument _turns backward_, in the sense opposite to the theoretic\nsense, and the explanation of its rotation, since discovered, is wholly\ndifferent. At last success came, by making the vacuum more complete, on\nthe one hand, and on the other by not blackening one of the faces of the\npaddles and directing a pencil of luminous rays upon one of the faces.\nThe radiometric effects and the other disturbing causes are eliminated\nby a series of pains-taking precautions, and one obtains a deviation\nwhich is very minute, but which is, it would seem, in conformity with\nthe theory.\n\nThe same effects of the Maxwell-Bartholi pressure are forecast likewise\nby the theory of Hertz of which we have before spoken, and by that of\nLorentz. But there is a difference. Suppose that the energy, under the\nform of light, for example, proceeds from a luminous source to any body\nthrough a transparent medium. The Maxwell-Bartholi pressure will act,\nnot alone upon the source at the departure, and on the body lit up at\nthe arrival, but upon the matter of the transparent medium which it\ntraverses. At the moment when the luminous wave reaches a new region of\nthis medium, this pressure will push forward the matter there\ndistributed and will put it back when the wave leaves this region. So\nthat the recoil of the source has for counterpart the forward movement\nof the transparent matter which is in contact with this source; a little\nlater, the recoil of this same matter has for counterpart the forward\nmovement of the transparent matter which lies a little further on, and\nso on.\n\nOnly, is the compensation perfect? Is the action of the Maxwell-Bartholi\npressure upon the matter of the transparent medium equal to its reaction\nupon the source, and that whatever be this matter? Or is this action by\nso much the less as the medium is less refractive and more rarefied,\nbecoming null in the void?\n\nIf we admit the theory of Hertz, who regards matter as mechanically\nbound to the ether, so that the ether may be entirely carried along by\nmatter, it would be necessary to answer yes to the first question and no\nto the second.\n\nThere would then be perfect compensation, as required by the principle\nof the equality of action and reaction, even in the least refractive\nmedia, even in the air, even in the interplanetary void, where it would\nsuffice to suppose a residue of matter, however subtile. If on the\ncontrary we admit the theory of Lorentz, the compensation, always\nimperfect, is insensible in the air and becomes null in the void.\n\nBut we have seen above that Fizeau's experiment does not permit of our\nretaining the theory of Hertz; it is necessary therefore to adopt the\ntheory of Lorentz, and consequently _to renounce the principle of\nreaction_.\n\n\nIV\n\n_Consequences of the Principle of Relativity_\n\nWe have seen above the reasons which impel us to regard the principle of\nrelativity as a general law of nature. Let us see to what consequences\nthis principle would lead, should it be regarded as finally\ndemonstrated.\n\nFirst, it obliges us to generalize the hypothesis of Lorentz and\nFitzgerald on the contraction of all bodies in the sense of the\ntranslation. In particular, we must extend this hypothesis to the\nelectrons themselves. Abraham considered these electrons as spherical\nand indeformable; it will be necessary for us to admit that these\nelectrons, spherical when in repose, undergo the Lorentz contraction\nwhen in motion and take then the form of flattened ellipsoids.\n\nThis deformation of the electrons will influence their mechanical\nproperties. In fact I have said that the displacement of these charged\nelectrons is a veritable current of convection and that their apparent\ninertia is due to the self-induction of this current: exclusively as\nconcerns the negative electrons; exclusively or not, we do not yet know,\nfor the positive electrons. Well, the deformation of the electrons, a\ndeformation which depends upon their velocity, will modify the\ndistribution of the electricity upon their surface, consequently the\nintensity of the convection current they produce, consequently the laws\naccording to which the self-induction of this current will vary as a\nfunction of the velocity.\n\nAt this price, the compensation will be perfect and will conform to the\nrequirements of the principle of relativity, but only upon two\nconditions:\n\n1\u00ba That the positive electrons have no real mass, but only a fictitious\nelectromagnetic mass; or at least that their real mass, if it exists, is\nnot constant and varies with the velocity according to the same laws as\ntheir fictitious mass;\n\n2\u00ba That all forces are of electromagnetic origin, or at least that they\nvary with the velocity according to the same laws as the forces of\nelectromagnetic origin.\n\nIt still is Lorentz who has made this remarkable synthesis; stop a\nmoment and see what follows therefrom. First, there is no more matter,\nsince the positive electrons no longer have real mass, or at least no\nconstant real mass. The present principles of our mechanics, founded\nupon the constancy of mass, must therefore be modified. Again, an\nelectromagnetic explanation must be sought of all the known forces, in\nparticular of gravitation, or at least the law of gravitation must be so\nmodified that this force is altered by velocity in the same way as the\nelectromagnetic forces. We shall return to this point.\n\nAll that appears, at first sight, a little artificial. In particular,\nthis deformation of electrons seems quite hypothetical. But the thing\nmay be presented otherwise, so as to avoid putting this hypothesis of\ndeformation at the foundation of the reasoning. Consider the electrons\nas material points and ask how their mass should vary as function of the\nvelocity not to contravene the principle of relativity. Or, still\nbetter, ask what should be their acceleration under the influence of an\nelectric or magnetic field, that this principle be not violated and that\nwe come back to the ordinary laws when we suppose the velocity very\nslight. We shall find that the variations of this mass, or of these\naccelerations, must be _as if_ the electron underwent the Lorentz\ndeformation.\n\n\nV\n\n_Kaufmann's Experiment_\n\nWe have before us, then, two theories: one where the electrons are\nindeformable, this is that of Abraham; the other where they undergo the\nLorentz deformation. In both cases, their mass increases with the\nvelocity, becoming infinite when this velocity becomes equal to that of\nlight; but the law of the variation is not the same. The method employed\nby Kaufmann to bring to light the law of variation of the mass seems\ntherefore to give us an experimental means of deciding between the two\ntheories.\n\nUnhappily, his first experiments were not sufficiently precise for that;\nso he decided to repeat them with more precautions, and measuring with\ngreat care the intensity of the fields. Under their new form _they are\nin favor of the theory of Abraham_. Then the principle of relativity\nwould not have the rigorous value we were tempted to attribute to it;\nthere would no longer be reason for believing the positive electrons\ndenuded of real mass like the negative electrons. However, before\ndefinitely adopting this conclusion, a little reflection is necessary.\nThe question is of such importance that it is to be wished Kaufmann's\nexperiment were repeated by another experimenter.[17] Unhappily, this\nexperiment is very delicate and could be carried out successfully only\nby a physicist of the same ability as Kaufmann. All precautions have\nbeen properly taken and we hardly see what objection could be made.\n\n [17] At the moment of going to press we learn that M. Bucherer has\n repeated the experiment, taking new precautions, and that he\n has obtained, contrary to Kaufmann, results confirming the\n views of Lorentz.\n\nThere is one point however to which I wish to draw attention: that is to\nthe measurement of the electrostatic field, a measurement upon which all\ndepends. This field was produced between the two armatures of a\ncondenser; and, between these armatures, there was to be made an\nextremely perfect vacuum, in order to obtain a complete isolation. Then\nthe difference of potential of the two armatures was measured, and the\nfield obtained by dividing this difference by the distance apart of the\narmatures. That supposes the field uniform; is this certain? Might there\nnot be an abrupt fall of potential in the neighborhood of one of the\narmatures, of the negative armature, for example? There may be a\ndifference of potential at the meeting of the metal and the vacuum, and\nit may be that this difference is not the same on the positive side and\non the negative side; what would lead me to think so is the electric\nvalve effects between mercury and vacuum. However slight the probability\nthat it is so, it seems that it should be considered.\n\n\nVI\n\n_The Principle of Inertia_\n\nIn the new dynamics, the principle of inertia is still true, that is to\nsay that an _isolated_ electron will have a straight and uniform motion.\nAt least this is generally assumed; however, Lindemann has made\nobjections to this view; I do not wish to take part in this discussion,\nwhich I can not here expound because of its too difficult character. In\nany case, slight modifications to the theory would suffice to shelter it\nfrom Lindemann's objections.\n\nWe know that a body submerged in a fluid experiences, when in motion,\nconsiderable resistance, but this is because our fluids are viscous; in\nan ideal fluid, perfectly free from viscosity, the body would stir up\nbehind it a liquid hill, a sort of wake; upon departure, a great effort\nwould be necessary to put it in motion, since it would be necessary to\nmove not only the body itself, but the liquid of its wake. But, the\nmotion once acquired, it would perpetuate itself without resistance,\nsince the body, in advancing, would simply carry with it the\nperturbation of the liquid, without the total vis viva of the liquid\naugmenting. Everything would happen therefore as if its inertia was\naugmented. An electron advancing in the ether would behave in the same\nway: around it, the ether would be stirred up, but this perturbation\nwould accompany the body in its motion; so that, for an observer carried\nalong with the electron, the electric and magnetic fields accompanying\nthis electron would appear invariable, and would change only if the\nvelocity of the electron varied. An effort would therefore be necessary\nto put the electron in motion, since it would be necessary to create the\nenergy of these fields; on the contrary, once the movement acquired, no\neffort would be necessary to maintain it, since the created energy would\nonly have to go along behind the electron as a wake. This energy,\ntherefore, could only augment the inertia of the electron, as the\nagitation of the liquid augments that of the body submerged in a perfect\nfluid. And anyhow, the negative electrons at least have no other inertia\nexcept that.\n\nIn the hypothesis of Lorentz, the vis viva, which is only the energy of\nthe ether, is not proportional to _v_^{2}. Doubtless if _v_ is very\nslight, the vis viva is sensibly proportional to _v_^{2}, the quantity\nof motion sensibly proportional to _v_, the two masses sensibly constant\nand equal to each other. But _when the velocity tends toward the\nvelocity of light, the vis viva, the quantity of motion and the two\nmasses increase beyond all limit_.\n\nIn the hypothesis of Abraham, the expressions are a little more\ncomplicated; but what we have just said remains true in essentials.\n\nSo the mass, the quantity of motion, the vis viva become infinite when\nthe velocity is equal to that of light.\n\nThence results that _no body can attain in any way a velocity beyond\nthat of light_. And in fact, in proportion as its velocity increases,\nits mass increases, so that its inertia opposes to any new increase of\nvelocity a greater and greater obstacle.\n\nA question then suggests itself: let us admit the principle of\nrelativity; an observer in motion would not have any means of perceiving\nhis own motion. If therefore no body in its absolute motion can exceed\nthe velocity of light, but may approach it as nearly as you choose, it\nshould be the same concerning its relative motion with reference to our\nobserver. And then we might be tempted to reason as follows: The\nobserver may attain a velocity of 200,000 kilometers; the body in its\nrelative motion with reference to the observer may attain the same\nvelocity; its absolute velocity will then be 400,000 kilometers, which\nis impossible, since this is beyond the velocity of light. This is only\na seeming, which vanishes when account is taken of how Lorentz evaluates\nlocal time.\n\n\nVII\n\n_The Wave of Acceleration_\n\nWhen an electron is in motion, it produces a perturbation in the ether\nsurrounding it; if its motion is straight and uniform, this perturbation\nreduces to the wake of which we have spoken in the preceding section.\nBut it is no longer the same, if the motion be curvilinear or varied.\nThe perturbation may then be regarded as the superposition of two\nothers, to which Langevin has given the names _wave of velocity_ and\n_wave of acceleration_. The wave of velocity is only the wave which\nhappens in uniform motion.\n\nAs to the wave of acceleration, this is a perturbation altogether\nanalogous to light waves, which starts from the electron at the instant\nwhen it undergoes an acceleration, and which is then propagated by\nsuccessive spherical waves with the velocity of light. Whence follows:\nin a straight and uniform motion, the energy is wholly conserved; but,\nwhen there is an acceleration, there is loss of energy, which is\ndissipated under the form of luminous waves and goes out to infinity\nacross the ether.\n\nHowever, the effects of this wave of acceleration, in particular the\ncorresponding loss of energy, are in most cases negligible, that is to\nsay not only in ordinary mechanics and in the motions of the heavenly\nbodies, but even in the radium rays, where the velocity is very great\nwithout the acceleration being so. We may then confine ourselves to\napplying the laws of mechanics, putting the force equal to the product\nof acceleration by mass, this mass, however, varying with the velocity\naccording to the laws explained above. We then say the motion is\n_quasi-stationary_.\n\nIt would not be the same in all cases where the acceleration is great,\nof which the chief are the following:\n\n1\u00ba In incandescent gases certain electrons take an oscillatory motion of\nvery high frequency; the displacements are very small, the velocities\nare finite, and the accelerations very great; energy is then\ncommunicated to the ether, and this is why these gases radiate light of\nthe same period as the oscillations of the electron;\n\n2\u00ba Inversely, when a gas receives light, these same electrons are put in\nswing with strong accelerations and they absorb light;\n\n3\u00ba In the Hertz discharger, the electrons which circulate in the\nmetallic mass undergo, at the instant of the discharge, an abrupt\nacceleration and take then an oscillatory motion of high frequency.\nThence results that a part of the energy radiates under the form of\nHertzian waves;\n\n4\u00ba In an incandescent metal, the electrons enclosed in this metal are\nimpelled with great velocity; upon reaching the surface of the metal,\nwhich they can not get through, they are reflected and thus undergo a\nconsiderable acceleration. This is why the metal emits light. The\ndetails of the laws of the emission of light by dark bodies are\nperfectly explained by this hypothesis;\n\n5\u00ba Finally when the cathode rays strike the anticathode, the negative\nelectrons, constituting these rays, which are impelled with very great\nvelocity, are abruptly arrested. Because of the acceleration they thus\nundergo, they produce undulations in the ether. This, according to\ncertain physicists, is the origin of the R\u00f6ntgen rays, which would only\nbe light rays of very short wave-length.\n\n\n\n\nCHAPTER III\n\nTHE NEW MECHANICS AND ASTRONOMY\n\n\nI\n\n_Gravitation_\n\nMass may be defined in two ways:\n\n1\u00ba By the quotient of the force by the acceleration; this is the true\ndefinition of the mass, which measures the inertia of the body.\n\n2\u00b0 By the attraction the body exercises upon an exterior body, in virtue\nof Newton's law. We should therefore distinguish the mass coefficient of\ninertia and the mass coefficient of attraction. According to Newton's\nlaw, there is rigorous proportionality between these two coefficients.\nBut that is demonstrated only for velocities to which the general\nprinciples of dynamics are applicable. Now, we have seen that the mass\ncoefficient of inertia increases with the velocity; should we conclude\nthat the mass coefficient of attraction increases likewise with the\nvelocity and remains proportional to the coefficient of inertia, or, on\nthe contrary, that this coefficient of attraction remains constant? This\nis a question we have no means of deciding.\n\nOn the other hand, if the coefficient of attraction depends upon the\nvelocity, since the velocities of two bodies which mutually attract are\nnot in general the same, how will this coefficient depend upon these two\nvelocities?\n\nUpon this subject we can only make hypotheses, but we are naturally led\nto investigate which of these hypotheses would be compatible with the\nprinciple of relativity. There are a great number of them; the only one\nof which I shall here speak is that of Lorentz, which I shall briefly\nexpound.\n\nConsider first electrons at rest. Two electrons of the same sign repel\neach other and two electrons of contrary sign attract each other; in the\nordinary theory, their mutual actions are proportional to their electric\ncharges; if therefore we have four electrons, two positive _A_ and\n_A'_, and two negative _B_ and _B'_, the charges of these four being the\nsame in absolute value, the repulsion of _A_ for _A'_ will be, at the\nsame distance, equal to the repulsion of _B_ for _B'_ and equal also to\nthe attraction of _A_ for _B'_, or of _A'_ for _B_. If therefore _A_ and\n_B_ are very near each other, as also _A'_ and _B'_, and we examine the\naction of the system _A_ + _B_ upon the system _A'_ + _B'_, we shall\nhave two repulsions and two attractions which will exactly compensate\neach other and the resulting action will be null.\n\nNow, material molecules should just be regarded as species of solar\nsystems where circulate the electrons, some positive, some negative, and\n_in such a way that the algebraic sum of all the charges is null_. A\nmaterial molecule is therefore wholly analogous to the system _A_ + _B_\nof which we have spoken, so that the total electric action of two\nmolecules one upon the other should be null.\n\nBut experiment shows us that these molecules attract each other in\nconsequence of Newtonian gravitation; and then we may make two\nhypotheses: we may suppose gravitation has no relation to the\nelectrostatic attractions, that it is due to a cause entirely different,\nand is simply something additional; or else we may suppose the\nattractions are not proportional to the charges and that the attraction\nexercised by a charge +1 upon a charge -1 is greater than the mutual\nrepulsion of two +1 charges, or two -1 charges.\n\nIn other words, the electric field produced by the positive electrons\nand that which the negative electrons produce might be superposed and\nyet remain distinct. The positive electrons would be more sensitive to\nthe field produced by the negative electrons than to the field produced\nby the positive electrons; the contrary would be the case for the\nnegative electrons. It is clear that this hypothesis somewhat\ncomplicates electrostatics, but that it brings back into it gravitation.\nThis was, in sum, Franklin's hypothesis.\n\nWhat happens now if the electrons are in motion? The positive electrons\nwill cause a perturbation in the ether and produce there an electric and\nmagnetic field. The same will be the case for the negative electrons.\nThe electrons, positive as well as negative, undergo then a mechanical\nimpulsion by the action of these different fields. In the ordinary\ntheory, the electromagnetic field, due to the motion of the positive\nelectrons, exercises, upon two electrons of contrary sign and of the\nsame absolute charge, equal actions with contrary sign. We may then\nwithout inconvenience not distinguish the field due to the motion of the\npositive electrons and the field due to the motion of the negative\nelectrons and consider only the algebraic sum of these two fields, that\nis to say the resulting field.\n\nIn the new theory, on the contrary, the action upon the positive\nelectrons of the electromagnetic field due to the positive electrons\nfollows the ordinary laws; it is the same with the action upon the\nnegative electrons of the field due to the negative electrons. Let us\nnow consider the action of the field due to the positive electrons upon\nthe negative electrons (or inversely); it will still follow the same\nlaws, but _with a different coefficient_. Each electron is more\nsensitive to the field created by the electrons of contrary name than to\nthe field created by the electrons of the same name.\n\nSuch is the hypothesis of Lorentz, which reduces to Franklin's\nhypothesis for slight velocities; it will therefore explain, for these\nsmall velocities, Newton's law. Moreover, as gravitation goes back to\nforces of electrodynamic origin, the general theory of Lorentz will\napply, and consequently the principle of relativity will not be\nviolated.\n\nWe see that Newton's law is no longer applicable to great velocities and\nthat it must be modified, for bodies in motion, precisely in the same\nway as the laws of electrostatics for electricity in motion.\n\nWe know that electromagnetic perturbations spread with the velocity of\nlight. We may therefore be tempted to reject the preceding theory upon\nremembering that gravitation spreads, according to the calculations of\nLaplace, at least ten million times more quickly than light, and that\nconsequently it can not be of electromagnetic origin. The result of\nLaplace is well known, but one is generally ignorant of its\nsignification. Laplace supposed that, if the propagation of gravitation\nis not instantaneous, its velocity of spread combines with that of the\nbody attracted, as happens for light in the phenomenon of astronomic\naberration, so that the effective force is not directed along the\nstraight joining the two bodies, but makes with this straight a small\nangle. This is a very special hypothesis, not well justified, and, in\nany case, entirely different from that of Lorentz. Laplace's result\nproves nothing against the theory of Lorentz.\n\n\nII\n\n_Comparison with Astronomic Observations_\n\nCan the preceding theories be reconciled with astronomic observations?\n\nFirst of all, if we adopt them, the energy of the planetary motions will\nbe constantly dissipated by the effect of the _wave of acceleration_.\nFrom this would result that the mean motions of the stars would\nconstantly accelerate, as if these stars were moving in a resistant\nmedium. But this effect is exceedingly slight, far too much so to be\ndiscerned by the most precise observations. The acceleration of the\nheavenly bodies is relatively slight, so that the effects of the wave of\nacceleration are negligible and the motion may be regarded as _quasi\nstationary_. It is true that the effects of the wave of acceleration\nconstantly accumulate, but this accumulation itself is so slow that\nthousands of years of observation would be necessary for it to become\nsensible. Let us therefore make the calculation considering the motion\nas quasi-stationary, and that under the three following hypotheses:\n\nA. Admit the hypothesis of Abraham (electrons indeformable) and retain\nNewton's law in its usual form;\n\nB. Admit the hypothesis of Lorentz about the deformation of electrons\nand retain the usual Newton's law;\n\nC. Admit the hypothesis of Lorentz about electrons and modify Newton's\nlaw as we have done in the preceding paragraph, so as to render it\ncompatible with the principle of relativity.\n\nIt is in the motion of Mercury that the effect will be most sensible,\nsince this planet has the greatest velocity. Tisserand formerly made an\nanalogous calculation, admitting Weber's law; I recall that Weber had\nsought to explain at the same time the electrostatic and electrodynamic\nphenomena in supposing that electrons (whose name was not yet invented)\nexercise, one upon another, attractions and repulsions directed along\nthe straight joining them, and depending not only upon their distances,\nbut upon the first and second derivatives of these distances,\nconsequently upon their velocities and their accelerations. This law of\nWeber, different enough from those which to-day tend to prevail, none\nthe less presents a certain analogy with them.\n\nTisserand found that, if the Newtonian attraction conformed to Weber's\nlaw there resulted, for Mercury's perihelion, secular variation of 14\",\n_of the same sense as that which has been observed and could not be\nexplained_, but smaller, since this is 38\".\n\nLet us recur to the hypotheses A, B and C, and study first the motion of\na planet attracted by a fixed center. The hypotheses B and C are no\nlonger distinguished, since, if the attracting point is fixed, the field\nit produces is a purely electrostatic field, where the attraction varies\ninversely as the square of the distance, in conformity with Coulomb's\nelectrostatic law, identical with that of Newton.\n\nThe vis viva equation holds good, taking for vis viva the new\ndefinition; in the same way, the equation of areas is replaced by\nanother equivalent to it; the moment of the quantity of motion is a\nconstant, but the quantity of motion must be defined as in the new\ndynamics.\n\nThe only sensible effect will be a secular motion of the perihelion.\nWith the theory of Lorentz, we shall find, for this motion, half of what\nWeber's law would give; with the theory of Abraham, two fifths.\n\nIf now we suppose two moving bodies gravitating around their common\ncenter of gravity, the effects are very little different, though the\ncalculations may be a little more complicated. The motion of Mercury's\nperihelion would therefore be 7\" in the theory of Lorentz and 5\".6 in\nthat of Abraham.\n\nThe effect moreover is proportional to (_n_^{3})(_a_^{2}), where _n_ is\nthe star's mean motion and a the radius of its orbit. For the planets,\nin virtue of Kepler's law, the effect varies then inversely as\nsqrt(_a_^{5}); it is therefore insensible, save for Mercury.\n\nIt is likewise insensible for the moon though _n_ is great, because _a_\nis extremely small; in sum, it is five times less for Venus, and six\nhundred times less for the moon than for Mercury. We may add that as to\nVenus and the earth, the motion of the perihelion (for the same angular\nvelocity of this motion) would be much more difficult to discern by\nastronomic observations, because the excentricity of their orbits is\nmuch less than for Mercury.\n\nTo sum up, _the only sensible effect upon astronomic observations would\nbe a motion of Mercury's perihelion, in the same sense as that which has\nbeen observed without being explained, but notably slighter_.\n\nThat can not be regarded as an argument in favor of the new dynamics,\nsince it will always be necessary to seek another explanation for the\ngreater part of Mercury's anomaly; but still less can it be regarded as\nan argument against it.\n\n\nIII\n\n_The Theory of Lesage_\n\nIt is interesting to compare these considerations with a theory long\nsince proposed to explain universal gravitation.\n\nSuppose that, in the interplanetary spaces, circulate in every\ndirection, with high velocities, very tenuous corpuscles. A body\nisolated in space will not be affected, apparently, by the impacts of\nthese corpuscles, since these impacts are equally distributed in all\ndirections. But if two bodies _A_ and _B_ are present, the body _B_ will\nplay the r\u00f4le of screen and will intercept part of the corpuscles which,\nwithout it, would have struck _A_. Then, the impacts received by _A_ in\nthe direction opposite that from _B_ will no longer have a counterpart,\nor will now be only partially compensated, and this will push _A_ toward\n_B_.\n\nSuch is the theory of Lesage; and we shall discuss it, taking first the\nview-point of ordinary mechanics.\n\nFirst, how should the impacts postulated by this theory take place; is\nit according to the laws of perfectly elastic bodies, or according to\nthose of bodies devoid of elasticity, or according to an intermediate\nlaw? The corpuscles of Lesage can not act as perfectly elastic bodies;\notherwise the effect would be null, since the corpuscles intercepted by\nthe body _B_ would be replaced by others which would have rebounded from\n_B_, and calculation proves that the compensation would be perfect. It\nis necessary then that the impact make the corpuscles lose energy, and\nthis energy should appear under the form of heat. But how much heat\nwould thus be produced? Note that attraction passes through bodies; it\nis necessary therefore to represent to ourselves the earth, for example,\nnot as a solid screen, but as formed of a very great number of very\nsmall spherical molecules, which play individually the r\u00f4le of little\nscreens, but between which the corpuscles of Lesage may freely\ncirculate. So, not only the earth is not a solid screen, but it is not\neven a cullender, since the voids occupy much more space than the\nplenums. To realize this, recall that Laplace has demonstrated that\nattraction, in traversing the earth, is weakened at most by one\nten-millionth part, and his proof is perfectly satisfactory: in fact, if\nattraction were absorbed by the body it traverses, it would no longer be\nproportional to the masses; it would be _relatively_ weaker for great\nbodies than for small, since it would have a greater thickness to\ntraverse. The attraction of the sun for the earth would therefore be\n_relatively_ weaker than that of the sun for the moon, and thence would\nresult, in the motion of the moon, a very sensible inequality. We should\ntherefore conclude, if we adopt the theory of Lesage, that the total\nsurface of the spherical molecules which compose the earth is at most\nthe ten-millionth part of the total surface of the earth.\n\nDarwin has proved that the theory of Lesage only leads exactly to\nNewton's law when we postulate particles entirely devoid of elasticity.\nThe attraction exerted by the earth on a mass 1 at a distance 1 will\nthen be proportional, at the same time, to the total surface _S_ of the\nspherical molecules composing it, to the velocity _v_ of the corpuscles,\nto the square root of the density [rho] of the medium formed by the\ncorpuscles. The heat produced will be proportional to _S_, to the\ndensity [rho], and to the cube of the velocity _v_.\n\nBut it is necessary to take account of the resistance experienced by a\nbody moving in such a medium; it can not move, in fact, without going\nagainst certain impacts, in fleeing, on the contrary, before those\ncoming in the opposite direction, so that the compensation realized in\nthe state of rest can no longer subsist. The calculated resistance is\nproportional to _S_, to [rho] and to _v_; now, we know that the heavenly\nbodies move as if they experienced no resistance, and the precision of\nobservations permits us to fix a limit to the resistance of the medium.\n\nThis resistance varying as _S_[rho]_v_, while the attraction varies as\n_S_{sqrt([rho]_v_)}, we see that the ratio of the resistance to the\nsquare of the attraction is inversely as the product _Sv_.\n\nWe have therefore a lower limit of the product _Sv_. We have already an\nupper limit of _S_ (by the absorption of attraction by the body it\ntraverses); we have therefore a lower limit of the velocity _v_, which\nmust be at least 24\u00b710^{17} times that of light.\n\nFrom this we are able to deduce [rho] and the quantity of heat produced;\nthis quantity would suffice to raise the temperature 10^{26} degrees a\nsecond; the earth would receive in a given time 10^{20} times more heat\nthan the sun emits in the same time; I am not speaking of the heat the\nsun sends to the earth, but of that it radiates in all directions.\n\nIt is evident the earth could not long stand such a r\u00e9gime.\n\nWe should not be led to results less fantastic if, contrary to Darwin's\nviews, we endowed the corpuscles of Lesage with an elasticity imperfect\nwithout being null. In truth, the vis viva of these corpuscles would not\nbe entirely converted into heat, but the attraction produced would\nlikewise be less, so that it would be only the part of this vis viva\nconverted into heat, which would contribute to produce the attraction\nand that would come to the same thing; a judicious employment of the\ntheorem of the viriel would enable us to account for this.\n\nThe theory of Lesage may be transformed; suppress the corpuscles and\nimagine the ether overrun in all senses by luminous waves coming from\nall points of space. When a material object receives a luminous wave,\nthis wave exercises upon it a mechanical action due to the\nMaxwell-Bartholi pressure, just as if it had received the impact of a\nmaterial projectile. The waves in question could therefore play the r\u00f4le\nof the corpuscles of Lesage. This is what is supposed, for example, by\nM. Tommasina.\n\nThe difficulties are not removed for all that; the velocity of\npropagation can be only that of light, and we are thus led, for the\nresistance of the medium, to an inadmissible figure. Besides, if the\nlight is all reflected, the effect is null, just as in the hypothesis of\nthe perfectly elastic corpuscles.\n\nThat there should be attraction, it is necessary that the light be\npartially absorbed; but then there is production of heat. The\ncalculations do not differ essentially from those made in the ordinary\ntheory of Lesage, and the result retains the same fantastic character.\n\nOn the other hand, attraction is not absorbed by the body it traverses,\nor hardly at all; it is not so with the light we know. Light which would\nproduce the Newtonian attraction would have to be considerably different\nfrom ordinary light and be, for example, of very short wave length. This\ndoes not count that, if our eyes were sensible of this light, the whole\nheavens should appear to us much more brilliant than the sun, so that\nthe sun would seem to us to stand out in black, otherwise the sun would\nrepel us instead of attracting us. For all these reasons, light which\nwould permit of the explanation of attraction would be much more like\nR\u00f6ntgen rays than like ordinary light.\n\nAnd besides, the X-rays would not suffice; however penetrating they may\nseem to us, they could not pass through the whole earth; it would be\nnecessary therefore to imagine X'-rays much more penetrating than the\nordinary X-rays. Moreover a part of the energy of these X'-rays would\nhave to be destroyed, otherwise there would be no attraction. If you do\nnot wish it transformed into heat, which would lead to an enormous heat\nproduction, you must suppose it radiated in every direction under the\nform of secondary rays, which might be called X'' and which would have\nto be much more penetrating still than the X'-rays, otherwise they would\nin their turn derange the phenomena of attraction.\n\nSuch are the complicated hypotheses to which we are led when we try to\ngive life to the theory of Lesage.\n\nBut all we have said presupposes the ordinary laws of mechanics.\n\nWill things go better if we admit the new dynamics? And first, can we\nconserve the principles of relativity? Let us give at first to the\ntheory of Lesage its primitive form, and suppose space ploughed by\nmaterial corpuscles; if these corpuscles were perfectly elastic, the\nlaws of their impact would conform to this principle of relativity, but\nwe know that then their effect would be null. We must therefore suppose\nthese corpuscles are not elastic, and then it is difficult to imagine a\nlaw of impact compatible with the principle of relativity. Besides, we\nshould still find a production of considerable heat, and yet a very\nsensible resistance of the medium.\n\nIf we suppress these corpuscles and revert to the hypothesis of the\nMaxwell-Bartholi pressure, the difficulties will not be less. This is\nwhat Lorentz himself has attempted in his Memoir to the Amsterdam\nAcademy of Sciences of April 25, 1900.\n\nConsider a system of electrons immersed in an ether permeated in every\nsense by luminous waves; one of these electrons, struck by one of these\nwaves, begins to vibrate; its vibration will be synchronous with that of\nlight; but it may have a difference of phase, if the electron absorbs a\npart of the incident energy. In fact, if it absorbs energy, this is\nbecause the vibration of the ether _impels_ the electron; the electron\nmust therefore be slower than the ether. An electron in motion is\nanalogous to a convection current; therefore every magnetic field, in\nparticular that due to the luminous perturbation itself, must exert a\nmechanical action upon this electron. This action is very slight;\nmoreover, it changes sign in the current of the period; nevertheless,\nthe mean action is not null if there is a difference of phase between\nthe vibrations of the electron and those of the ether. The mean action\nis proportional to this difference, consequently to the energy absorbed\nby the electron. I can not here enter into the detail of the\ncalculations; suffice it to say only that the final result is an\nattraction of any two electrons, varying inversely as the square of the\ndistance and proportional to the energy absorbed by the two electrons.\n\nTherefore there can not be attraction without absorption of light and,\nconsequently, without production of heat, and this it is which\ndetermined Lorentz to abandon this theory, which, at bottom, does not\ndiffer from that of Lesage-Maxwell-Bartholi. He would have been much\nmore dismayed still if he had pushed the calculation to the end. He\nwould have found that the temperature of the earth would have to\nincrease 10^{12} degrees a second.\n\n\nIV\n\n_Conclusions_\n\nI have striven to give in few words an idea as complete as possible of\nthese new doctrines; I have sought to explain how they took birth;\notherwise the reader would have had ground to be frightened by their\nboldness. The new theories are not yet demonstrated; far from it; only\nthey rest upon an aggregate of probabilities sufficiently weighty for us\nnot to have the right to treat them with disregard.\n\nNew experiments will doubtless teach us what we should finally think of\nthem. The knotty point of the question lies in Kaufmann's experiment and\nthose that may be undertaken to verify it.\n\nIn conclusion, permit me a word of warning. Suppose that, after some\nyears, these theories undergo new tests and triumph; then our secondary\neducation will incur a great danger; certain professors will doubtless\nwish to make a place for the new theories.\n\nNovelties are so attractive, and it is so hard not to seem highly\nadvanced! At least there will be the wish to open vistas to the pupils\nand, before teaching them the ordinary mechanics, to let them know it\nhas had its day and was at best good enough for that old dolt Laplace.\nAnd then they will not form the habit of the ordinary mechanics.\n\nIs it well to let them know this is only approximative? Yes; but later,\nwhen it has penetrated to their very marrow, when they shall have taken\nthe bent of thinking only through it, when there shall no longer be risk\nof their unlearning it, then one may, without inconvenience, show them\nits limits.\n\nIt is with the ordinary mechanics that they must live; this alone will\nthey ever have to apply. Whatever be the progress of automobilism, our\nvehicles will never attain speeds where it is not true. The other is\nonly a luxury, and we should think of the luxury only when there is no\nlonger any risk of harming the necessary.\n\n\n\n\nBOOK IV\n\n\nASTRONOMIC SCIENCE\n\n\n\n\nCHAPTER I\n\nTHE MILKY WAY AND THE THEORY OF GASES\n\n\nThe considerations to be here developed have scarcely as yet drawn the\nattention of astronomers; there is hardly anything to cite except an\ningenious idea of Lord Kelvin's, which has opened a new field of\nresearch, but still waits to be followed out. Nor have I original\nresults to impart, and all I can do is to give an idea of the problems\npresented, but which no one hitherto has undertaken to solve. Every one\nknows how a large number of modern physicists represent the constitution\nof gases; gases are formed of an innumerable multitude of molecules\nwhich, at high speeds, cross and crisscross in every direction. These\nmolecules probably act at a distance one upon another, but this action\ndecreases very rapidly with distance, so that their trajectories remain\nsensibly straight; they cease to be so only when two molecules happen to\npass very near to each other; in this case, their mutual attraction or\nrepulsion makes them deviate to right or left. This is what is sometimes\ncalled an impact; but the word _impact_ is not to be understood in its\nusual sense; it is not necessary that the two molecules come into\ncontact, it suffices that they approach sufficiently near each other for\ntheir mutual attractions to become sensible. The laws of the deviation\nthey undergo are the same as for a veritable impact.\n\nIt seems at first that the disorderly impacts of this innumerable dust\ncan engender only an inextricable chaos before which analysis must\nrecoil. But the law of great numbers, that supreme law of chance, comes\nto our aid; in presence of a semi-disorder, we must despair, but in\nextreme disorder, this statistical law reestablishes a sort of mean\norder where the mind can recover. It is the study of this mean order\nwhich constitutes the kinetic theory of gases; it shows us that the\nvelocities of the molecules are equally distributed among all the\ndirections, that the rapidity of these velocities varies from one\nmolecule to another, but that even this variation is subject to a law\ncalled Maxwell's law. This law tells us how many of the molecules move\nwith such and such a velocity. As soon as the gas departs from this law,\nthe mutual impacts of the molecules, in modifying the rapidity and\ndirection of their velocities, tend to bring it promptly back.\nPhysicists have striven, not without success, to explain in this way the\nexperimental properties of gases; for example Mariotte's law.\n\nConsider now the milky way; there also we see an innumerable dust; only\nthe grains of this dust are not atoms, they are stars; these grains move\nalso with high velocities; they act at a distance one upon another, but\nthis action is so slight at great distance that their trajectories are\nstraight; and yet, from time to time, two of them may approach near\nenough to be deviated from their path, like a comet which has passed too\nnear Jupiter. In a word, to the eyes of a giant for whom our suns would\nbe as for us our atoms, the milky way would seem only a bubble of gas.\n\nSuch was Lord Kelvin's leading idea. What may be drawn from this\ncomparison? In how far is it exact? This is what we are to investigate\ntogether; but before reaching a definite conclusion, and without wishing\nto prejudge it, we foresee that the kinetic theory of gases will be for\nthe astronomer a model he should not follow blindly, but from which he\nmay advantageously draw inspiration. Up to the present, celestial\nmechanics has attacked only the solar system or certain systems of\ndouble stars. Before the assemblage presented by the milky way, or the\nagglomeration of stars, or the resolvable nebulae it recoils, because it\nsees therein only chaos. But the milky way is not more complicated than\na gas; the statistical methods founded upon the calculus of\nprobabilities applicable to a gas are also applicable to it. Before all,\nit is important to grasp the resemblance of the two cases, and their\ndifference.\n\nLord Kelvin has striven to determine in this manner the dimensions of\nthe milky way; for that we are reduced to counting the stars visible in\nour telescopes; but we are not sure that behind the stars we see, there\nare not others we do not see; so that what we should measure in this way\nwould not be the size of the milky way, it would be the range of our\ninstruments.\n\nThe new theory comes to offer us other resources. In fact, we know the\nmotions of the stars nearest us, and we can form an idea of the rapidity\nand direction of their velocities. If the ideas above set forth are\nexact, these velocities should follow Maxwell's law, and their mean\nvalue will tell us, so to speak, that which corresponds to the\ntemperature of our fictitious gas. But this temperature depends itself\nupon the dimensions of our gas bubble. In fact, how will a gaseous mass\nlet loose in the void act, if its elements attract one another according\nto Newton's law? It will take a spherical form; moreover, because of\ngravitation, the density will be greater at the center, the pressure\nalso will increase from the surface to the center because of the weight\nof the outer parts drawn toward the center; finally, the temperature\nwill increase toward the center: the temperature and the pressure being\nconnected by the law called adiabatic, as happens in the successive\nlayers of our atmosphere. At the surface itself, the pressure will be\nnull, and it will be the same with the absolute temperature, that is to\nsay with the velocity of the molecules.\n\nA question comes here: I have spoken of the adiabatic law, but this law\nis not the same for all gases, since it depends upon the ratio of their\ntwo specific heats; for the air and like gases, this ratio is 1.42; but\nis it to air that it is proper to liken the milky way? Evidently not, it\nshould be regarded as a mono-atomic gas, like mercury vapor, like argon,\nlike helium, that is to say that the ratio of the specific heats should\nbe taken equal to 1.66. And, in fact, one of our molecules would be for\nexample the solar system; but the planets are very small personages, the\nsun alone counts, so that our molecule is indeed mono-atomic. And even\nif we take a double star, it is probable that the action of a strange\nstar which might approach it would become sufficiently sensible to\ndeviate the motion of general translation of the system much before\nbeing able to trouble the relative orbits of the two components; the\ndouble star, in a word, would act like an indivisible atom.\n\nHowever that may be, the pressure, and consequently the temperature, at\nthe center of the gaseous sphere would be by so much the greater as the\nsphere was larger since the pressure increases by the weight of all the\nsuperposed layers. We may suppose that we are nearly at the center of\nthe milky way, and by observing the mean proper velocity of the stars,\nwe shall know that which corresponds to the central temperature of our\ngaseous sphere and we shall determine its radius.\n\nWe may get an idea of the result by the following considerations: make a\nsimpler hypothesis: the milky way is spherical, and in it the masses are\ndistributed in a homogeneous manner; thence results that the stars in it\ndescribe ellipses having the same center. If we suppose the velocity\nbecomes nothing at the surface, we may calculate this velocity at the\ncenter by the equation of vis viva. Thus we find that this velocity is\nproportional to the radius of the sphere and to the square root of its\ndensity. If the mass of this sphere was that of the sun and its radius\nthat of the terrestrial orbit, this velocity would be (it is easy to\nsee) that of the earth in its orbit. But in the case we have supposed,\nthe mass of the sun should be distributed in a sphere of radius\n1,000,000 times greater, this radius being the distance of the nearest\nstars; the density is therefore 10^{18} times less; now, the velocities\nare of the same order, therefore it is necessary that the radius be\n10^{9} times greater, be 1,000 times the distance of the nearest stars,\nwhich would give about a thousand millions of stars in the milky way.\n\nBut you will say these hypothesis differ greatly from the reality;\nfirst, the milky way is not spherical and we shall soon return to this\npoint, and again the kinetic theory of gases is not compatible with the\nhypothesis of a homogeneous sphere. But in making the exact calculation\naccording to this theory, we should find a different result, doubtless,\nbut of the same order of magnitude; now in such a problem the data are\nso uncertain that the order of magnitude is the sole end to be aimed at.\n\nAnd here a first remark presents itself; Lord Kelvin's result, which I\nhave obtained again by an approximative calculation, agrees sensibly\nwith the evaluations the observers have made with their telescopes; so\nthat we must conclude we are very near to piercing through the milky\nway. But that enables us to answer another question. There are the stars\nwe see because they shine; but may there not be dark stars circulating\nin the interstellar spaces whose existence might long remain unknown?\nBut then, what Lord Kelvin's method would give us would be the total\nnumber of stars, including the dark stars; as his figure is comparable\nto that the telescope gives, this means there is no dark matter, or at\nleast not so much as of shining matter.\n\nBefore going further, we must look at the problem from another angle. Is\nthe milky way thus constituted truly the image of a gas properly so\ncalled? You know Crookes has introduced the notion of a fourth state of\nmatter, where gases having become too rarefied are no longer true gases\nand become what he calls radiant matter. Considering the slight density\nof the milky way, is it the image of gaseous matter or of radiant\nmatter? The consideration of what is called the _free path_ will furnish\nus the answer.\n\nThe trajectory of a gaseous molecule may be regarded as formed of\nstraight segments united by very small arcs corresponding to the\nsuccessive impacts. The length of each of these segments is what is\ncalled the free path; of course this length is not the same for all the\nsegments and for all the molecules; but we may take a mean; this is what\nis called the _mean path_. This is the greater the less the density of\nthe gas. The matter will be radiant if the mean path is greater than the\ndimensions of the receptacle wherein the gas is enclosed, so that a\nmolecule has a chance to go across the whole receptacle without\nundergoing an impact; if the contrary be the case, it is gaseous. From\nthis it follows that the same fluid may be radiant in a little\nreceptacle and gaseous in a big one; this perhaps is why, in a Crookes\ntube, it is necessary to make the vacuum by so much the more complete as\nthe tube is larger.\n\nHow is it then for the milky way? This is a mass of gas of which the\ndensity is very slight, but whose dimensions are very great; has a star\nchances of traversing it without undergoing an impact, that is to say\nwithout passing sufficiently near another star to be sensibly deviated\nfrom its route! What do we mean by _sufficiently near_? That is perforce\na little arbitrary; take it as the distance from the sun to Neptune,\nwhich would represent a deviation of a dozen degrees; suppose therefore\neach of our stars surrounded by a protective sphere of this radius;\ncould a straight pass between these spheres? At the mean distance of the\nstars of the milky way, the radius of these spheres will be seen under\nan angle of about a tenth of a second; and we have a thousand millions\nof stars. Put upon the celestial sphere a thousand million little\ncircles of a tenth of a second radius. Are the chances that these\ncircles will cover a great number of times the celestial sphere? Far\nfrom it; they will cover only its sixteen thousandth part. So the milky\nway is not the image of gaseous matter, but of Crookes' radiant matter.\nNevertheless, as our foregoing conclusions are happily not at all\nprecise, we need not sensibly modify them.\n\nBut there is another difficulty: the milky way is not spherical, and we\nhave reasoned hitherto as if it were, since this is the form of\nequilibrium a gas isolated in space would take. To make amends,\nagglomerations of stars exist whose form is globular and to which would\nbetter apply what we have hitherto said. Herschel has already endeavored\nto explain their remarkable appearances. He supposed the stars of the\naggregates uniformly distributed, so that an assemblage is a homogeneous\nsphere; each star would then describe an ellipse and all these orbits\nwould be passed over in the same time, so that at the end of a period\nthe aggregate would take again its primitive configuration and this\nconfiguration would be stable. Unluckily, the aggregates do not appear\nto be homogeneous; we see a condensation at the center, we should\nobserve it even were the sphere homogeneous, since it is thicker at the\ncenter; but it would not be so accentuated. We may therefore rather\ncompare an aggregate to a gas in adiabatic equilibrium, which takes the\nspherical form because this is the figure of equilibrium of a gaseous\nmass.\n\nBut, you will say, these aggregates are much smaller than the milky way,\nof which they even in probability make part, and even though they be\nmore dense, they will rather present something analogous to radiant\nmatter; now, gases attain their adiabatic equilibrium only through\ninnumerable impacts of the molecules. That might perhaps be adjusted.\nSuppose the stars of the aggregate have just enough energy for their\nvelocity to become null when they reach the surface; then they may\ntraverse the aggregate without impact, but arrived at the surface they\nwill go back and will traverse it anew; after a great number of\ncrossings, they will at last be deviated by an impact; under these\nconditions, we should still have a matter which might be regarded as\ngaseous; if perchance there had been in the aggregate stars whose\nvelocity was greater, they have long gone away out of it, they have left\nit never to return. For all these reasons, it would be interesting to\nexamine the known aggregates, to seek to account for the law of the\ndensities, and to see if it is the adiabatic law of gases.\n\nBut to return to the milky way; it is not spherical and would rather be\nrepresented as a flattened disc. It is clear then that a mass starting\nwithout velocity from the surface will reach the center with different\nvelocities, according as it starts from the surface in the neighborhood\nof the middle of the disc or just on the border of the disc; the\nvelocity would be notably greater in the latter case. Now, up to the\npresent, we have supposed that the proper velocities of the stars, those\nwe observe, must be comparable to those which like masses would attain;\nthis involves a certain difficulty. We have given above a value for the\ndimensions of the milky way, and we have deduced it from the observed\nproper velocities which are of the same order of magnitude as that of\nthe earth in its orbit; but which is the dimension we have thus\nmeasured? Is it the thickness? Is it the radius of the disc? It is\ndoubtless something intermediate; but what can we say then of the\nthickness itself, or of the radius of the disc? Data are lacking to make\nthe calculation; I shall confine myself to giving a glimpse of the\npossibility of basing an evaluation at least approximate upon a deeper\ndiscussion of the proper motions.\n\nAnd then we find ourselves facing two hypotheses: either the stars of\nthe milky way are impelled by velocities for the most part parallel to\nthe galactic plane, but otherwise distributed uniformly in all\ndirections parallel to this plane. If this be so, observation of the\nproper motions should show a preponderance of components parallel to the\nmilky way; this is to be determined, because I do not know whether a\nsystematic discussion has ever been made from this view-point. On the\nother hand, such an equilibrium could only be provisory, since because\nof impacts the molecules, I mean the stars, would in the long run\nacquire notable velocities in the sense perpendicular to the milky way\nand would end by swerving from its plane, so that the system would tend\ntoward the spherical form, the only figure of equilibrium of an isolated\ngaseous mass.\n\nOr else the whole system is impelled by a common rotation, and for that\nreason is flattened like the earth, like Jupiter, like all bodies that\ntwirl. Only, as the flattening is considerable, the rotation must be\nrapid; rapid doubtless, but it must be understood in what sense this\nword is used. The density of the milky way is 10^{23} times less than\nthat of the sun; a velocity of rotation sqrt(10^{25}) times less than\nthat of the sun, for it would, therefore, be the equivalent so far as\nconcerns flattening; a velocity 10^{12} times slower than that of the\nearth, say a thirtieth of a second of arc in a century, would be a very\nrapid rotation, almost too rapid for stable equilibrium to be possible.\n\nIn this hypothesis, the observable proper motions would appear to us\nuniformly distributed, and there would no longer be a preponderance of\ncomponents parallel to the galactic plane.\n\nThey will tell us nothing about the rotation itself, since we belong to\nthe turning system. If the spiral nebul\u00e6 are other milky ways, foreign\nto ours, they are not borne along in this rotation, and we might study\ntheir proper motions. It is true they are very far away; if a nebula has\nthe dimensions of the milky way and if its apparent radius is for\nexample 20\", its distance is 10,000 times the radius of the milky way.\n\nBut that makes no difference, since it is not about the translation of\nour system that we ask information from them, but about its rotation.\nThe fixed stars, by their apparent motion, reveal to us the diurnal\nrotation of the earth, though their distance is immense. Unluckily, the\npossible rotation of the milky way, however rapid it may be relatively,\nis very slow viewed absolutely, and besides the pointings on nebul\u00e6 can\nnot be very precise; therefore thousands of years of observations would\nbe necessary to learn anything.\n\nHowever that may be, in this second hypothesis, the figure of the milky\nway would be a figure of final equilibrium.\n\nI shall not further discuss the relative value of these two hypotheses\nsince there is a third which is perhaps more probable. We know that\namong the irresolvable nebul\u00e6, several kinds may be distinguished: the\nirregular nebul\u00e6 like that of Orion, the planetary and annular nebul\u00e6,\nthe spiral nebul\u00e6. The spectra of the first two families have been\ndetermined, they are discontinuous; these nebul\u00e6 are therefore not\nformed of stars; besides, their distribution on the heavens seems to\ndepend upon the milky way; whether they have a tendency to go away from\nit, or on the contrary to approach it, they make therefore a part of the\nsystem. On the other hand, the spiral nebul\u00e6 are generally considered as\nindependent of the milky way; it is supposed that they, like it, are\nformed of a multitude of stars, that they are, in a word, other milky\nways very far away from ours. The recent investigations of Stratonoff\ntend to make us regard the milky way itself as a spiral nebula, and this\nis the third hypothesis of which I wish to speak.\n\nHow can we explain the very singular appearances presented by the spiral\nnebul\u00e6, which are too regular and too constant to be due to chance?\nFirst of all, to take a look at one of these representations is enough\nto see that the mass is in rotation; we may even see what the sense of\nthe rotation is; all the spiral radii are curved in the same sense; it\nis evident that the _moving wing_ lags behind the pivot and that fixes\nthe sense of the rotation. But this is not all; it is evident that these\nnebul\u00e6 can not be likened to a gas at rest, nor even to a gas in\nrelative equilibrium under the sway of a uniform rotation; they are to\nbe compared to a gas in permanent motion in which internal currents\nprevail.\n\nSuppose, for example, that the rotation of the central nucleus is rapid\n(you know what I mean by this word), too rapid for stable equilibrium;\nthen at the equator the centrifugal force will drive it away over the\nattraction, and the stars will tend to break away at the equator and\nwill form divergent currents; but in going away, as their moment of\nrotation remains constant, while the radius vector augments, their\nangular velocity will diminish, and this is why the moving wing seems to\nlag back.\n\nFrom this point of view, there would not be a real permanent motion, the\ncentral nucleus would constantly lose matter which would go out of it\nnever to return, and would drain away progressively. But we may modify\nthe hypothesis. In proportion as it goes away, the star loses its\nvelocity and ends by stopping; at this moment attraction regains\npossession of it and leads it back toward the nucleus; so there will be\ncentripetal currents. We must suppose the centripetal currents are the\nfirst rank and the centrifugal currents the second rank, if we adopt the\ncomparison with a troop in battle executing a change of front; and, in\nfact, it is necessary that the composite centrifugal force be\ncompensated by the attraction exercised by the central layers of the\nswarm upon the extreme layers.\n\nBesides, at the end of a certain time a permanent r\u00e9gime establishes\nitself; the swarm being curved, the attraction exercised upon the pivot\nby the moving wing tends to slow up the pivot and that of the pivot upon\nthe moving wing tends to accelerate the advance of this wing which no\nlonger augments its lag, so that finally all the radii end by turning\nwith a uniform velocity. We may still suppose that the rotation of the\nnucleus is quicker than that of the radii.\n\nA question remains; why do these centripetal and centrifugal swarms tend\nto concentrate themselves in radii instead of disseminating themselves a\nlittle everywhere? Why do these rays distribute themselves regularly? If\nthe swarms concentrate themselves, it is because of the attraction\nexercised by the already existing swarms upon the stars which go out\nfrom the nucleus in their neighborhood. After an inequality is produced,\nit tends to accentuate itself in this way.\n\nWhy do the rays distribute themselves regularly? That is less obvious.\nSuppose there is no rotation, that all the stars are in two planes at\nright angles, in such a way that their distribution is symmetric with\nregard to these two planes.\n\nBy symmetry, there would be no reason for their going out of these\nplanes, nor for the symmetry changing. This configuration would give us\ntherefore equilibrium, but _this would be an unstable equilibrium_.\n\nIf on the contrary, there is rotation, we shall find an analogous\nconfiguration of equilibrium with four curved rays, equal to each other\nand intersecting at 90\u00b0, and if the rotation is sufficiently rapid, this\nequilibrium is stable.\n\nI am not in position to make this more precise: enough if you see that\nthese spiral forms may perhaps some day be explained by only the law of\ngravitation and statistical consideration recalling those of the theory\nof gases.\n\nWhat has been said of internal currents shows it is of interest to\ndiscuss systematically the aggregate of proper motions; this may be done\nin a hundred years, when the second edition is issued of the chart of\nthe heavens and compared with the first, that we now are making.\n\nBut, in conclusion, I wish to call your attention to a question, that of\nthe age of the milky way or the nebul\u00e6. If what we think we see is\nconfirmed, we can get an idea of it. That sort of statistical\nequilibrium of which gases give us the model is established only in\nconsequence of a great number of impacts. If these impacts are rare, it\ncan come about only after a very long time; if really the milky way (or\nat least the agglomerations which are contained in it), if the nebul\u00e6\nhave attained this equilibrium, this means they are very old, and we\nshall have an inferior limit of their age. Likewise we should have of it\na superior limit; this equilibrium is not final and can not last always.\nOur spiral nebul\u00e6 would be comparable to gases impelled by permanent\nmotions; but gases in motion are viscous and their velocities end by\nwearing out. What here corresponds to the viscosity (and which depends\nupon the chances of impact of the molecules) is excessively slight, so\nthat the present r\u00e9gime may persist during an extremely long time, yet\nnot forever, so that our milky ways can not live eternally nor become\ninfinitely old.\n\nAnd this is not all. Consider our atmosphere: at the surface must reign\na temperature infinitely small and the velocity of the molecules there\nis near zero. But this is a question only of the mean velocity; as a\nconsequence of impacts, one of these molecules may acquire (rarely, it\nis true) an enormous velocity, and then it will rush out of the\natmosphere, and once out, it will never return; therefore our atmosphere\ndrains off thus with extreme slowness. The milky way also from time to\ntime loses a star by the same mechanism, and that likewise limits its\nduration.\n\nWell, it is certain that if we compute in this manner the age of the\nmilky way, we shall get enormous figures. But here a difficulty presents\nitself. Certain physicists, relying upon other considerations, reckon\nthat suns can have only an ephemeral existence, about fifty million\nyears; our minimum would be much greater than that. Must we believe that\nthe evolution of the milky way began when the matter was still dark? But\nhow have the stars composing it reached all at the same time adult age,\nan age so briefly to endure? Or must they reach there all successively,\nand are those we see only a feeble minority compared with those\nextinguished or which shall one day light up? But how reconcile that\nwith what we have said above on the absence of a noteworthy proportion\nof dark matter? Should we abandon one of the two hypotheses, and which?\nI confine myself to pointing out the difficulty without pretending to\nsolve it; I shall end therefore with a big interrogation point.\n\nHowever, it is interesting to set problems, even when their solution\nseems very far away.\n\n\n\n\nCHAPTER II\n\nFRENCH GEODESY\n\n\nEvery one understands our interest in knowing the form and dimensions of\nour earth; but some persons will perhaps be surprised at the exactitude\nsought after. Is this a useless luxury? What good are the efforts so\nexpended by the geodesist?\n\nShould this question be put to a congressman, I suppose he would say:\n\"I am led to believe that geodesy is one of the most useful of the\nsciences; because it is one of those costing us most dear.\" I shall try\nto give you an answer a little more precise.\n\nThe great works of art, those of peace as well as those of war, are not\nto be undertaken without long studies which save much groping,\nmiscalculation and useless expense. These studies can only be based upon\na good map. But a map will be only a valueless phantasy if constructed\nwithout basing it upon a solid framework. As well make stand a human\nbody minus the skeleton.\n\nNow, this framework is given us by geodesic measurements; so, without\ngeodesy, no good map; without a good map, no great public works.\n\nThese reasons will doubtless suffice to justify much expense; but these\nare arguments for practical men. It is not upon these that it is proper\nto insist here; there are others higher and, everything considered, more\nimportant.\n\nSo we shall put the question otherwise; can geodesy aid us the better to\nknow nature? Does it make us understand its unity and harmony? In\nreality an isolated fact is of slight value, and the conquests of\nscience are precious only if they prepare for new conquests.\n\nIf therefore a little hump were discovered on the terrestrial ellipsoid,\nthis discovery would be by itself of no great interest. On the other\nhand, it would become precious if, in seeking the cause of this hump, we\nhoped to penetrate new secrets.\n\nWell, when, in the eighteenth century, Maupertuis and La Condamine\nbraved such opposite climates, it was not solely to learn the shape of\nour planet, it was a question of the whole world-system.\n\nIf the earth was flattened, Newton triumphed and with him the doctrine\nof gravitation and the whole modern celestial mechanics.\n\nAnd to-day, a century and a half after the victory of the Newtonians,\nthink you geodesy has nothing more to teach us?\n\nWe know not what is within our globe. The shafts of mines and borings\nhave let us know a layer of 1 or 2 kilometers thickness, that is to say,\nthe millionth part of the total mass; but what is beneath?\n\nOf all the extraordinary journeys dreamed by Jules Verne, perhaps that\nto the center of the earth took us to regions least explored.\n\nBut these deep-lying rocks we can not reach, exercise from afar their\nattraction which operates upon the pendulum and deforms the terrestrial\nspheroid. Geodesy can therefore weigh them from afar, so to speak, and\ntell us of their distribution. Thus will it make us really see those\nmysterious regions which Jules Verne only showed us in imagination.\n\nThis is not an empty illusion. M. Faye, comparing all the measurements,\nhas reached a result well calculated to surprise us. Under the oceans,\nin the depths, are rocks of very great density; under the continents, on\nthe contrary, are empty spaces.\n\nNew observations will modify perhaps the details of these conclusions.\n\nIn any case, our venerated dean has shown us where to search and what\nthe geodesist may teach the geologist, desirous of knowing the interior\nconstitution of the earth, and even the thinker wishing to speculate\nupon the past and the origin of this planet.\n\nAnd now, why have I entitled this chapter _French Geodesy_? It is\nbecause, in each country, this science has taken, more than all others,\nperhaps, a national character. It is easy to see why.\n\nThere must be rivalry. The scientific rivalries are always courteous, or\nat least almost always; in any case, they are necessary, because they\nare always fruitful. Well, in those enterprises which require such long\nefforts and so many collaborators, the individual is effaced, in spite\nof himself, of course; no one has the right to say: this is my work.\nTherefore it is not between men, but between nations that rivalries go\non.\n\nSo we are led to seek what has been the part of France. Her part I\nbelieve we are right to be proud of.\n\nAt the beginning of the eighteenth century, long discussions arose\nbetween the Newtonians who believed the earth flattened, as the theory\nof gravitation requires, and Cassini, who, deceived by inexact\nmeasurements, believed our globe elongated. Only direct observation\ncould settle the question. It was our Academy of Sciences that undertook\nthis task, gigantic for the epoch.\n\nWhile Maupertuis and Clairaut measured a degree of meridian under the\npolar circle, Bouguer and La Condamine went toward the Andes Mountains,\nin regions then under Spain which to-day are the Republic of Ecuador.\n\nOur envoys were exposed to great hardships. Traveling was not as easy as\nat present.\n\nTruly, the country where Maupertuis operated was not a desert and he\neven enjoyed, it is said, among the Laplanders those sweet satisfactions\nof the heart that real arctic voyagers never know. It was almost the\nregion where, in our days, comfortable steamers carry, each summer,\nhosts of tourists and young English people. But in those days Cook's\nagency did not exist and Maupertuis really believed he had made a polar\nexpedition.\n\nPerhaps he was not altogether wrong. The Russians and the Swedes carry\nout to-day analogous measurements at Spitzbergen, in a country where\nthere is real ice-cap. But they have quite other resources, and the\ndifference of time makes up for that of latitude.\n\nThe name of Maupertuis has reached us much scratched by the claws of\nDoctor Akakia; the scientist had the misfortune to displease Voltaire,\nwho was then the king of mind. He was first praised beyond measure; but\nthe flatteries of kings are as much to be dreaded as their displeasure,\nbecause the days after are terrible. Voltaire himself knew something of\nthis.\n\nVoltaire called Maupertuis, my amiable master in thinking, marquis of\nthe polar circle, dear flattener out of the world and Cassini, and even,\nflattery supreme, Sir Isaac Maupertuis; he wrote him: \"Only the king of\nPrussia do I put on a level with you; he only lacks being a geometer.\"\nBut soon the scene changes, he no longer speaks of deifying him, as in\ndays of yore the Argonauts, or of calling down from Olympus the council\nof the gods to contemplate his works, but of chaining him up in a\nmadhouse. He speaks no longer of his sublime mind, but of his despotic\npride, plated with very little science and much absurdity.\n\nI care not to relate these comico-heroic combats; but permit me some\nreflections on two of Voltaire's verses. In his 'Discourse on\nModeration' (no question of moderation in praise and criticism), the\npoet has written:\n\n You have confirmed in regions drear\n What Newton discerned without going abroad.\n\nThese two verses (which replace the hyperbolic praises of the first\nperiod) are very unjust, and doubtless Voltaire was too enlightened not\nto know it.\n\nThen, only those discoveries were esteemed which could be made without\nleaving one's house.\n\nTo-day, it would rather be theory that one would make light of.\n\nThis is to misunderstand the aim of science.\n\nIs nature governed by caprice, or does harmony rule there? That is the\nquestion. It is when it discloses to us this harmony that science is\nbeautiful and so worthy to be cultivated. But whence can come to us this\nrevelation, if not from the accord of a theory with experiment? To seek\nwhether this accord exists or if it fails, this therefore is our aim.\nConsequently these two terms, which we must compare, are as\nindispensable the one as the other. To neglect one for the other would\nbe nonsense. Isolated, theory would be empty, experiment would be blind;\neach would be useless and without interest.\n\nMaupertuis therefore deserves his share of glory. Truly, it will not\nequal that of Newton, who had received the spark divine; nor even that\nof his collaborator Clairaut. Yet it is not to be despised, because his\nwork was necessary, and if France, outstripped by England in the\nseventeenth century, has so well taken her revenge in the century\nfollowing, it is not alone to the genius of Clairauts, d'Alemberts,\nLaplaces that she owes it; it is also to the long patience of the\nMaupertuis and the La Condamines.\n\nWe reach what may be called the second heroic period of geodesy. France\nis torn within. All Europe is armed against her; it would seem that\nthese gigantic combats might absorb all her forces. Far from it; she\nstill has them for the service of science. The men of that time recoiled\nbefore no enterprise, they were men of faith.\n\nDelambre and M\u00e9chain were commissioned to measure an arc going from\nDunkerque to Barcelona. This time there was no going to Lapland or to\nPeru; the hostile squadrons had closed to us the ways thither. But,\nthough the expeditions are less distant, the epoch is so troubled that\nthe obstacles, the perils even, are just as great.\n\nIn France, Delambre had to fight against the ill-will of suspicious\nmunicipalities. One knows that the steeples, which are visible from so\nfar, and can be aimed at with precision, often serve as signal points to\ngeodesists. But in the region Delambre traversed there were no longer\nany steeples. A certain proconsul had passed there, and boasted of\nknocking down all the steeples rising proudly above the humble abode of\nthe sans-culottes. Pyramids then were built of planks and covered with\nwhite cloth to make them more visible. That was quite another thing:\nwith white cloth! What was this rash person who, upon our heights so\nrecently set free, dared to raise the hateful standard of the\ncounter-revolution? It was necessary to border the white cloth with blue\nand red bands.\n\nM\u00e9chain operated in Spain; the difficulties were other; but they were\nnot less. The Spanish peasants were hostile. There steeples were not\nlacking: but to install oneself in them with mysterious and perhaps\ndiabolic instruments, was it not sacrilege? The revolutionists were\nallies of Spain, but allies smelling a little of the stake.\n\n\"Without cease,\" writes M\u00e9chain, \"they threaten to butcher us.\"\nFortunately, thanks to the exhortations of the priests, to the pastoral\nletters of the bishops, these ferocious Spaniards contented themselves\nwith threatening.\n\nSome years after M\u00e9chain made a second expedition into Spain: he\nproposed to prolong the meridian from Barcelona to the Balearics. This\nwas the first time it had been attempted to make the triangulations\noverpass a large arm of the sea by observing signals installed upon some\nhigh mountain of a far-away isle. The enterprise was well conceived and\nwell prepared; it failed however.\n\nThe French scientist encountered all sorts of difficulties of which he\ncomplains bitterly in his correspondence. \"Hell,\" he writes, perhaps\nwith some exaggeration--\"hell and all the scourges it vomits upon the\nearth, tempests, war, the plague and black intrigues are therefore\nunchained against me!\"\n\nThe fact is that he encountered among his collaborators more of proud\nobstinacy than of good will and that a thousand accidents retarded his\nwork. The plague was nothing, the fear of the plague was much more\nredoubtable; all these isles were on their guard against the neighboring\nisles and feared lest they should receive the scourge from them. M\u00e9chain\nobtained permission to disembark only after long weeks upon the\ncondition of covering all his papers with vinegar; this was the\nantisepsis of that time.\n\nDisgusted and sick, he had just asked to be recalled, when he died.\n\nArago and Biot it was who had the honor of taking up the unfinished work\nand carrying it on to completion.\n\nThanks to the support of the Spanish government, to the protection of\nseveral bishops and, above all, to that of a famous brigand chief, the\noperations went rapidly forward. They were successfully completed, and\nBiot had returned to France when the storm burst.\n\nIt was the moment when all Spain took up arms to defend her independence\nagainst France. Why did this stranger climb the mountains to make\nsignals? It was evidently to call the French army. Arago was able to\nescape the populace only by becoming a prisoner. In his prison, his only\ndistraction was reading in the Spanish papers the account of his own\nexecution. The papers of that time sometimes gave out news prematurely.\nHe had at least the consolation of learning that he died with courage\nand like a Christian.\n\nEven the prison was no longer safe; he had to escape and reach Algiers.\nThere, he embarked for Marseilles on an Algerian vessel. This ship was\ncaptured by a Spanish corsair, and behold Arago carried back to Spain\nand dragged from dungeon to dungeon, in the midst of vermin and in the\nmost shocking wretchedness.\n\nIf it had only been a question of his subjects and his guests, the dey\nwould have said nothing. But there were on board two lions, a present\nfrom the African sovereign to Napoleon. The dey threatened war.\n\nThe vessel and the prisoners were released. The port should have been\nproperly reached, since they had on board an astronomer; but the\nastronomer was seasick, and the Algerian seamen, who wished to make\nMarseilles, came out at Bougie. Thence Arago went to Algiers, traversing\nKabylia on foot in the midst of a thousand perils. He was long detained\nin Africa and threatened with the convict prison. Finally he was able to\nget back to France; his observations, which he had preserved and\nsafeguarded under his shirt, and, what is still more remarkable, his\ninstruments had traversed unhurt these terrible adventures. Up to this\npoint, not only did France hold the foremost place, but she occupied the\nstage almost alone.\n\nIn the years which follow, she has not been inactive and our\nstaff-office map is a model. However, the new methods of observation and\ncalculation have come to us above all from Germany and England. It is\nonly in the last forty years that France has regained her rank. She owes\nit to a scientific officer, General Perrier, who has successfully\nexecuted an enterprise truly audacious, the junction of Spain and\nAfrica. Stations were installed on four peaks upon the two sides of the\nMediterranean. For long months they awaited a calm and limpid\natmosphere. At last was seen the little thread of light which had\ntraversed 300 kilometers over the sea. The undertaking had succeeded.\n\nTo-day have been conceived projects still more bold. From a mountain\nnear Nice will be sent signals to Corsica, not now for geodesic\ndeterminations, but to measure the velocity of light. The distance is\nonly 200 kilometers; but the ray of light is to make the journey there\nand return, after reflection by a mirror installed in Corsica. And it\nshould not wander on the way, for it must return exactly to the point of\ndeparture.\n\nEver since, the activity of French geodesy has never slackened. We have\nno more such astonishing adventures to tell; but the scientific work\naccomplished is immense. The territory of France beyond the sea, like\nthat of the mother country, is covered by triangles measured with\nprecision.\n\nWe have become more and more exacting and what our fathers admired does\nnot satisfy us to-day. But in proportion as we seek more exactitude, the\ndifficulties greatly increase; we are surrounded by snares and must be\non our guard against a thousand unsuspected causes of error. It is\nneedful, therefore, to create instruments more and more faultless.\n\nHere again France has not let herself be distanced. Our appliances for\nthe measurement of bases and angles leave nothing to desire, and, I may\nalso mention the pendulum of Colonel Defforges, which enables us to\ndetermine gravity with a precision hitherto unknown.\n\nThe future of French geodesy is at present in the hands of the\nGeographic Service of the army, successively directed by General Bassot\nand General Berthaut. We can not sufficiently congratulate ourselves\nupon it. For success in geodesy, scientific aptitudes are not enough; it\nis necessary to be capable of standing long fatigues in all sorts of\nclimates; the chief must be able to win obedience from his collaborators\nand to make obedient his native auxiliaries. These are military\nqualities. Besides, one knows that, in our army, science has always\nmarched shoulder to shoulder with courage.\n\nI add that a military organization assures the indispensable unity of\naction. It would be more difficult to reconcile the rival pretensions of\nscientists jealous of their independence, solicitous of what they call\ntheir fame, and who yet must work in concert, though separated by great\ndistances. Among the geodesists of former times there were often\ndiscussions, of which some aroused long echoes. The Academy long\nresounded with the quarrel of Bouguer and La Condamine. I do not mean to\nsay that soldiers are exempt from passion, but discipline imposes\nsilence upon a too sensitive self-esteem.\n\nSeveral foreign governments have called upon our officers to organize\ntheir geodesic service: this is proof that the scientific influence of\nFrance abroad has not declined.\n\nOur hydrographic engineers contribute also to the common achievement a\nglorious contingent. The survey of our coasts, of our colonies, the\nstudy of the tides, offer them a vast domain of research. Finally I may\nmention the general leveling of France which is carried out by the\ningenious and precise methods of M. Lallemand.\n\nWith such men we are sure of the future. Moreover, work for them will\nnot be lacking; our colonial empire opens for them immense expanses illy\nexplored. That is not all: the International Geodetic Association has\nrecognized the necessity of a new measurement of the arc of Quito,\ndetermined in days of yore by La Condamine. It is France that has been\ncharged with this operation; she had every right to it, since our\nancestors had made, so to speak, the scientific conquest of the\nCordilleras. Besides, these rights have not been contested and our\ngovernment has undertaken to exercise them.\n\nCaptains Maurain and Lacombe completed a first reconnaissance, and the\nrapidity with which they accomplished their mission, crossing the\nroughest regions and climbing the most precipitous summits, is worthy of\nall praise. It won the admiration of General Alfaro, President of the\nRepublic of Ecuador, who called them 'los hombres de hierro,' the men of\niron.\n\nThe final commission then set out under the command of\nLieutenant-Colonel (then Major) Bourgeois. The results obtained have\njustified the hopes entertained. But our officers have encountered\nunforeseen difficulties due to the climate. More than once, one of them\nhas been forced to remain several months at an altitude of 4,000 meters,\nin the clouds and the snow, without seeing anything of the signals he\nhad to aim at and which refused to unmask themselves. But thanks to\ntheir perseverance and courage, there resulted from this only a delay\nand an increase of expense, without the exactitude of the measurements\nsuffering therefrom.\n\n\n\n\nGENERAL CONCLUSIONS\n\n\nWhat I have sought to explain in the preceding pages is how the\nscientist should guide himself in choosing among the innumerable facts\noffered to his curiosity, since indeed the natural limitations of his\nmind compel him to make a choice, even though a choice be always a\nsacrifice. I have expounded it first by general considerations,\nrecalling on the one hand the nature of the problem to be solved and on\nthe other hand seeking to better comprehend that of the human mind,\nwhich is the principal instrument of the solution. I then have explained\nit by examples; I have not multiplied them indefinitely; I also have had\nto make a choice, and I have chosen naturally the questions I had\nstudied most. Others would doubtless have made a different choice; but\nwhat difference, because I believe they would have reached the same\nconclusions.\n\nThere is a hierarchy of facts; some have no reach; they teach us nothing\nbut themselves. The scientist who has ascertained them has learned\nnothing but a fact, and has not become more capable of foreseeing new\nfacts. Such facts, it seems, come once, but are not destined to\nreappear.\n\nThere are, on the other hand, facts of great yield; each of them teaches\nus a new law. And since a choice must be made, it is to these that the\nscientist should devote himself.\n\nDoubtless this classification is relative and depends upon the weakness\nof our mind. The facts of slight outcome are the complex facts, upon\nwhich various circumstances may exercise a sensible influence,\ncircumstances too numerous and too diverse for us to discern them all.\nBut I should rather say that these are the facts we think complex, since\nthe intricacy of these circumstances surpasses the range of our mind.\nDoubtless a mind vaster and finer than ours would think differently of\nthem. But what matter; we can not use that superior mind, but only our\nown.\n\nThe facts of great outcome are those we think simple; may be they really\nare so, because they are influenced only by a small number of\nwell-defined circumstances, may be they take on an appearance of\nsimplicity because the various circumstances upon which they depend obey\nthe laws of chance and so come to mutually compensate. And this is what\nhappens most often. And so we have been obliged to examine somewhat more\nclosely what chance is.\n\nFacts where the laws of chance apply become easy of access to the\nscientist who would be discouraged before the extraordinary complication\nof the problems where these laws are not applicable. We have seen that\nthese considerations apply not only to the physical sciences, but to the\nmathematical sciences. The method of demonstration is not the same for\nthe physicist and the mathematician. But the methods of invention are\nvery much alike. In both cases they consist in passing up from the fact\nto the law, and in finding the facts capable of leading to a law.\n\nTo bring out this point, I have shown the mind of the mathematician at\nwork, and under three forms: the mind of the mathematical inventor and\ncreator; that of the unconscious geometer who among our far distant\nancestors, or in the misty years of our infancy, has constructed for us\nour instinctive notion of space; that of the adolescent to whom the\nteachers of secondary education unveil the first principles of the\nscience, seeking to give understanding of the fundamental definitions.\nEverywhere we have seen the r\u00f4le of intuition and of the spirit of\ngeneralization without which these three stages of mathematicians, if I\nmay so express myself, would be reduced to an equal impotence.\n\nAnd in the demonstration itself, the logic is not all; the true\nmathematical reasoning is a veritable induction, different in many\nregards from the induction of physics, but proceeding like it from the\nparticular to the general. All the efforts that have been made to\nreverse this order and to carry back mathematical induction to the rules\nof logic have eventuated only in failures, illy concealed by the\nemployment of a language inaccessible to the uninitiated. The examples I\nhave taken from the physical sciences have shown us very different cases\nof facts of great outcome. An experiment of Kaufmann on radium rays\nrevolutionizes at the same time mechanics, optics and astronomy. Why?\nBecause in proportion as these sciences have developed, we have the\nbetter recognized the bonds uniting them, and then we have perceived a\nspecies of general design of the chart of universal science. There are\nfacts common to several sciences, which seem the common source of\nstreams diverging in all directions and which are comparable to that\nknoll of Saint Gothard whence spring waters which fertilize four\ndifferent valleys.\n\nAnd then we can make choice of facts with more discernment than our\npredecessors who regarded these valleys as distinct and separated by\nimpassable barriers.\n\nIt is always simple facts which must be chosen, but among these simple\nfacts we must prefer those which are situated upon these sorts of knolls\nof Saint Gothard of which I have just spoken.\n\nAnd when sciences have no direct bond, they still mutually throw light\nupon one another by analogy. When we studied the laws obeyed by gases we\nknew we had attacked a fact of great outcome; and yet this outcome was\nstill estimated beneath its value, since gases are, from a certain point\nof view, the image of the milky way, and those facts which seemed of\ninterest only for the physicist, ere long opened new vistas to astronomy\nquite unexpected.\n\nAnd finally when the geodesist sees it is necessary to move his\ntelescope some seconds to see a signal he has set up with great pains,\nthis is a very small fact; but this is a fact of great outcome, not only\nbecause this reveals to him the existence of a small protuberance upon\nthe terrestrial globe, that little hump would be by itself of no great\ninterest, but because this protuberance gives him information about the\ndistribution of matter in the interior of the globe, and through that\nabout the past of our planet, about its future, about the laws of its\ndevelopment.\n\n\n * * * * *\n\n\n\n\nINDEX\n\n\n aberration of light, 315, 496\n\n Abraham, 311, 490-1, 505-7, 509, 515-6\n\n absolute motion, 107\n orientation, 83\n space, 85, 93, 246, 257, 353\n\n acceleration, 94, 98, 486, 509\n\n accidental constant, 112\n errors, 171, 402\n\n accommodation of the eyes, 67-8\n\n action at a distance, 137\n\n addition, 34\n\n aim of mathematics, 280\n\n alchemists, 11\n\n Alfaro, 543\n\n algebra, 379\n\n analogy, 220\n\n analysis, 218-9, 279\n\n analysis situs, 53, 239, 381\n\n analyst, 210, 221\n\n ancestral experience, 91\n\n Andrade, 93, 104, 228\n\n Andrews, 153\n\n angle sum of triangle, 58\n\n Anglo-Saxons, 3\n\n antinomies, 449, 457, 477\n\n Arago, 540-1\n\n Aristotle, 205, 292, 460\n\n arithmetic, 34, 379, 441, 463\n\n associativity, 35\n\n assumptions, 451, 453\n\n astronomy, 81, 289, 315, 512\n\n Atwood, 446\n\n axiom, 60, 63, 65, 215\n\n\n Bacon, 128\n\n Bartholi, 503\n\n Bassot, 542\n\n beauty, 349, 368\n\n Becquerel, 312\n\n Beltrami, 56, 58\n\n Bergson, 321\n\n Berkeley, 4\n\n Berthaut, 542\n\n Bertrand, 156, 190, 211, 395\n\n Betti, 239\n\n Biot, 540\n\n bodies, solid, 72\n\n Boltzmann, 304\n\n Bolyai, 56, 201, 203\n\n Borel, 482\n\n Bouguer, 537, 542\n\n Bourgeois, 543\n\n Boutroux, 390, 464\n\n Bradley, 496\n\n Briot, 298\n\n Brownian movement, 152, 410\n\n Bucherer, 507\n\n Burali-Forti, 457-9, 477, 481-2\n\n\n Caen, 387-8\n\n Calinon, 228\n\n canal rays, 491-2\n\n canals, semicircular, 276\n\n Cantor, 11, 448-9, 457, 459, 477\n\n Cantorism, 381, 382, 480, 484\n\n capillarity, 298\n\n Carlyle, 128\n\n Carnot's principle, 143, 151, 300, 303-5, 399\n\n Cassini, 537\n\n cathode rays, 487-92\n\n cells, 217\n\n center of gravity, 103\n\n central forces, 297\n\n Chaldeans, 290\n\n chance, 395, 408\n\n change of position, 70\n state, 70\n\n chemistry of the stars, 295\n\n circle-squarers, 11\n\n Clairaut, 537-8\n\n Clausius, 119, 123, 143\n\n color sensation, 252\n\n Columbus, 228\n\n commutativity, 35-6\n\n compensation, 72\n\n complete induction, 40\n\n Comte, 294\n\n Condorcet, 411\n\n contingence, 340\n\n continuity, 173\n\n continuum, 43\n amorphous, 238\n mathematical, 46\n physical, 46, 240\n tridimensional, 240\n\n convention, 50, 93, 106, 125, 173, 208, 317, 440, 451\n\n convergence, 67-8\n\n coordinates, 244\n\n Copernicus, 109, 291, 354\n\n Coulomb, 143, 516\n\n Couturat, 450, 453, 456, 460, 462-3, 467, 472-6\n\n creation, mathematical, 383\n\n creed, 1\n\n Cr\u00e9mieu, 168-9, 490\n\n crisis, 303\n\n Crookes, 195, 488, 527-8\n\n crude fact, 326, 330\n\n Curie, 312-3, 318\n\n current, 186\n\n curvature, 58-9\n\n curve, 213, 346\n\n curves without tangents, 51\n\n cut, 52, 256\n\n cyclones, 353\n\n\n d'Alembert, 538\n\n Darwin, 518-9\n\n De Cyon, 276, 427\n\n Dedekind, 44-5\n\n Defforges, 542\n\n definitions, 430, 453\n\n deformation, 73, 415\n\n Delage, 277\n\n Delambre, 539\n\n Delbeuf, 414\n\n Descartes, 127\n\n determinism, 123, 340\n\n dictionary, 59\n\n didymium, 333\n\n dilatation, 76\n\n dimensions, 53, 68, 78, 241, 256, 426\n\n direction, 69\n\n Dirichlet, 213\n\n dispersion, 141\n\n displacement, 73, 77, 247, 256\n\n distance, 59, 292\n\n distributivity, 36\n\n Du Bois-Reymond, 50\n\n\n earth, rotation of, 326, 353\n\n eclipse, 326\n\n electricity, 174\n\n electrified bodies, 117\n\n electrodynamic attraction, 308\n induction, 188\n mass, 311\n\n electrodynamics, 184, 282\n\n electromagnetic theory of light, 301\n\n electrons, 316, 492-4, 505-8, 510, 512-4\n\n elephant, 217, 436\n\n ellipse, 215\n\n Emerson, 203\n\n empiricism, 86, 271\n\n Epimenides, 478-9\n\n equation of Laplace, 283\n\n Erd\u00e9ly, 203\n\n errors, accidental, 171, 402\n law of, 119\n systematic, 171, 402\n theory of, 402, 406\n\n ether, 145, 351\n\n ethics, 205\n\n Euclid, 62, 86, 202-3, 213\n\n Euclidean geometry, 65, 235-6, 337\n\n Euclid's postulate, 83, 91, 124, 353, 443, 453, 468, 470-1\n\n experience, 90-1\n\n experiment, 127, 317, 336, 446\n\n\n fact, crude, 326, 330\n in the rough, 327\n scientific, 326\n\n facts, 362, 371\n\n Fahrenheit, 238\n\n Faraday, 150, 192\n\n Faye, 536\n\n Fechner, 46, 52\n\n Fehr, 383\n\n finite, 57\n\n Fitzgerald, 415-6, 500-1, 505\n\n Fizeau, 146, 149, 309, 498, 504\n\n Flammarion, 400, 406-7\n\n flattening of the earth, 353\n\n force, 72, 98, 444\n direction of, 445\n -flow, 284\n\n forces, central, 297\n equivalence of, 445\n magnitude of, 445\n\n Foucault's pendulum, 85, 109, 353\n\n four dimensions, 78\n\n Fourier, 298-9\n\n Fourier's problem, 317\n series, 286\n\n Franklin, 513-4\n\n Fresnel, 132, 140, 153, 174, 176, 181, 351, 498\n\n Fuchsian, 387-8\n\n function, 213\n continuous, 218, 288\n\n\n Galileo, 97, 331, 353-4\n\n gaseous pressure, 141\n\n gases, theory of, 400, 405, 523\n\n Gauss, 384-5, 406\n\n Gay-Lussac, 157\n\n generalize, 342\n\n geodesy, 535\n\n geometer, 83, 210, 438\n\n geometric space, 66\n\n geometry, 72, 81, 125, 207, 380, 428, 442, 467\n Euclidean, 65, 93\n fourth, 62\n non-Euclidean, 55\n projective, 201\n qualitative, 238\n rational, 5, 467\n Riemann's, 57\n spheric, 59\n\n Gibbs, 304\n\n Goldstein, 492\n\n Gouy, 152, 305, 410\n\n gravitation, 512\n\n Greeks, 93, 368\n\n\n Hadamard, 459\n\n Halsted, 3, 203, 464, 467\n\n Hamilton, 115\n\n helium, 294\n\n Helmholtz, 56, 115, 118, 141, 190, 196\n\n Hercules, 449\n\n Hermite, 211, 220, 222, 285\n\n Herschel, 528\n\n Hertz, 102, 145, 194-5, 427, 488, 498, 502, 504, 510\n\n Hertzian oscillator, 309, 317\n\n Hilbert, 5, 11, 203, 433, 450-1, 464-8, 471, 475-7, 484\n\n Himstedt, 195\n\n Hipparchus, 291\n\n homogeneity, 74, 423\n\n homogeneous, 67\n\n hydrodynamics, 284\n\n hyperbola, 215\n\n hypotheses, 6, 15, 127, 133\n\n hysteresis, 151\n\n\n identity of spaces, 268\n of two points, 259\n\n illusions, optical, 202\n\n incommensurable numbers, 44\n\n induction, complete, 40, 452-3, 467-8\n electromagnetic, 188\n mathematical, 40, 220\n principle of, 481\n\n inertia, 93, 486, 489, 507\n\n infinite, 448\n\n infinitesimals, 50\n\n inquisitor, 331\n\n integration, 139\n\n interpolation, 131\n\n intuition, 210, 213, 215\n\n invariant, 333\n\n Ionians, 127\n\n ions, 152\n\n irrational number, 44\n\n irreversible phenomena, 151\n\n isotropic, 67\n\n\n Japanese mice, 277, 427\n\n Jevons, 451\n\n John Lackland, 128\n\n Jules Verne, 111, 536\n\n Jupiter, 131, 157, 231, 289\n\n\n Kant, 16, 64, 202-3, 450-1, 471\n\n Kauffman, 311, 490-1, 495, 506-7, 522, 545\n\n Kazan, 203\n\n Kelvin, 145, 523-4, 526-7\n\n Kepler, 120, 133, 153, 282, 291-2\n\n Kepler's laws, 136, 516\n\n kinematics, 337\n\n kinetic energy, 116\n theory of gases, 141\n\n Kirchhoff, 98-9, 103-5\n\n Klein, 60, 211, 287\n\n knowledge, 201\n\n K\u00f6nig, 144, 477\n\n Kovalevski, 212, 286\n\n Kronecker, 44\n\n\n Lacombe, 543\n\n La Condamine, 535, 537-8, 542-3\n\n Lagrange, 98, 151, 179\n\n Laisant, 383\n\n Lallamand, 543\n\n Langevin, 509\n\n Laplace, 298, 398, 514-5, 518, 522, 538\n\n Laplace's equation, 283, 287\n\n Larmor, 145, 150\n\n Lavoisier's principle, 301, 310, 312\n\n law, 207, 291, 395\n\n Leibnitz, 32, 450, 471\n\n Le Roy, 28, 321-6, 332, 335, 337, 347-8, 354, 468\n\n Lesage, 517-21\n\n Liard, 440\n\n Lie, 62-3, 212\n\n light sensations, 252\n theory of, 351\n velocity of, 232, 312\n\n Lindemann, 508\n\n line, 203, 243\n\n linkages, 144\n\n Lippmann, 196\n\n Lobachevski, 29, 56, 60, 62, 83, 86, 203\n\n Lobachevski's space, 239\n\n local time, 306-7, 499\n\n logic, 214, 435, 448, 460-2, 464\n\n logistic, 457, 472-4\n\n logisticians, 472\n\n Lorentz, 147, 149, 196-7, 306, 308, 311, 315, 415-6, 492, 498-502,\n 504-9, 512, 514-6, 521\n\n Lotze, 264\n\n luck, 399\n\n Lumen, 407-8\n\n\n MacCullagh, 150\n\n Mach, 375\n\n Mach-Delage, 276\n\n magnetism, 149\n\n magnitude, 49\n\n Mariotte's law, 120, 132, 157, 342, 524\n\n Maros, 203\n\n mass, 98, 312, 446, 486, 489, 494, 515\n\n mathematical analysis, 218\n continuum, 46\n creation, 383\n induction, 40, 220\n physics, 136, 297, 319\n\n mathematics, 369, 448\n\n matter, 492\n\n Maupertuis, 535, 537-8\n\n Maurain, 543\n\n Maxwell, 140, 152, 175, 177, 181, 193, 282-3, 298, 301, 304-5, 351,\n 503, 524-5\n\n Maxwell-Bartholi, 309, 503-4, 519, 521\n\n Mayer, 119, 123, 300, 312, 318\n\n measurement, 49\n\n M\u00e9chain, 539-40\n\n mechanical explanation, 177\n mass, 312\n\n mechanics, 92, 444, 486, 496, 512\n anthropomorphic, 103\n celestial, 279\n statistical, 304\n\n M\u00e9ray, 211\n\n metaphysician, 221\n\n meteorology, 398\n\n mice, 277\n\n Michelson, 306, 309, 311, 316, 498, 500-1\n\n milky way, 523-30\n\n Mill, Stuart, 60-1, 453-4\n\n Monist, 4, 89, 464\n\n moons of Jupiter, 233\n\n Morley, 309\n\n motion of liquids, 283\n of moon, 28\n of planets, 341\n relative, 107, 487\n without deformation, 236\n\n multiplication, 36\n\n muscular sensations, 69\n\n\n Nagaoka, 317\n\n nature, 127\n\n navigation, 289\n\n neodymium, 333\n\n neomonics, 283\n\n Neumann, 181\n\n Newton, 85, 96, 98, 109, 153, 291, 370, 486, 516, 536, 538\n\n Newton's argument, 108, 334, 343\n law, 111, 118, 132, 136, 149, 157, 233, 282, 292, 512, 514-5,\n 518, 525\n principle, 146, 300, 308-9, 312\n\n no-class theory, 478\n\n nominalism, 28, 125, 321, 333, 335\n\n non-Euclidean geometry, 55, 59, 388\n language, 127\n space, 55, 235, 237\n straight, 236, 470\n world, 75\n\n number, 31\n big, 88\n imaginary, 283\n incommensurable, 44\n transfinite, 448-9\n whole, 44, 469\n\n\n objectivity, 209, 347, 349, 408\n\n optical illusions, 202\n\n optics, 174, 496\n\n orbit of Saturn, 341\n\n order, 385\n\n orientation, 83\n\n osmotic, 141\n\n\n Padoa, 463\n\n Panth\u00e9on, 414\n\n parallax, 470\n\n parallels, 56, 443\n\n Paris time, 233\n\n parry, 419-22, 427\n\n partition, 45\n\n pasigraphy, 456-7\n\n Pasteur, 128\n\n Peano, 450, 456-9, 463, 472\n\n Pender, 490\n\n pendulum, 224\n\n Perrier, 541\n\n Perrin, 195\n\n phosphorus, 333, 468, 470-1\n\n physical continuum, 46\n\n physics, 127, 140, 144, 279, 297\n\n physics of central forces, 297\n of the principles, 299\n\n Pieri, 11, 203\n\n Plato, 292\n\n Poincar\u00e9, 473\n\n point, 89, 244\n\n Poncelet, 215\n\n postulates, 382\n\n potential energy, 116\n\n praseodymium, 333\n\n principle, 125, 299\n Carnot's, 143, 151, 300, 303-5, 399\n Clausius', 119, 123, 143\n Hamilton's, 115\n Lavoisier's, 300, 310\n Mayer's, 119, 121, 123, 300, 312, 318\n Newton's, 146, 300, 308-9, 312\n of action and reaction, 300, 487, 502\n of conservation of energy, 300\n of degradation of energy, 300\n of inertia, 93, 486, 507\n of least action, 118, 300\n of relativity, 300, 305, 498, 505\n\n Prony, 445\n\n psychologist, 383\n\n Ptolemy, 110, 291, 353-4\n\n Pythagoras, 292\n\n\n quadrature of the circle, 161\n\n qualitative geometry, 238\n space, 207\n time, 224\n\n quaternions, 282\n\n\n radiometer, 503\n\n radium, 312, 318, 486-7\n\n Rados, 201\n\n Ramsay, 313\n\n rational geometry, 5, 467\n\n reaction, 502\n\n reality, 217, 340, 349\n\n R\u00e9aumur, 238\n\n recurrence, 37\n\n Regnault, 170\n\n relativity, 83, 305, 417, 423, 498, 505\n\n Richard, 477-8, 480-1\n\n Riemann, 56, 62, 145, 212, 239, 243, 381, 432\n surface, 211, 287\n\n Roemer, 233\n\n R\u00f6ntgen, 511, 520\n\n rotation of earth, 225, 331, 353\n\n roulette, 403\n\n Rowland, 194-7, 305, 489\n\n Royce, 202\n\n Russell, 201, 450, 460-2, 464-7, 471-4, 477-82, 484-5\n\n\n St. Louis exposition, 208, 320\n\n Sarcey, 442\n\n Saturn, 231, 317\n\n Schiller, 202\n\n Schliemann, 19\n\n science, 205, 321, 323, 340, 354\n\n Science and Hypothesis, 205-7, 220, 240, 246-7, 319, 353, 452\n\n semicircular canals, 276\n\n series, development in, 287\n Fourier's, 286\n\n Sirius, 226, 229\n\n solid bodies, 72\n\n space, 55, 66, 89, 235, 256\n absolute, 85, 93\n amorphous, 417\n Bolyai, 56\n Euclidean, 65\n geometric, 66\n Lobachevski's, 239\n motor, 69\n non-Euclidean, 55, 235, 237\n of four dimensions, 78\n perceptual, 66, 69\n tactile, 68, 264\n visual, 67, 252\n\n spectra, 316\n\n spectroscope, 294\n\n Spencer, 9\n\n sponge, 219\n\n Stallo, 10\n\n stars, 292\n\n statistical mechanics, 304\n\n straight, 62, 82, 236, 433, 450, 470\n\n Stratonoff, 531\n\n surfaces, 58\n\n systematic errors, 171\n\n\n tactile space, 68, 264\n\n Tait, 98\n\n tangent, 51\n\n Tannery, 43\n\n teaching, 430, 437\n\n thermodynamics, 115, 119\n\n Thomson, 98, 488\n\n thread, 104\n\n time, 223\n equality, 225\n local, 306, 307\n measure of, 223-4\n\n Tisserand, 515-6\n\n Tolstoi, 354, 362, 368\n\n Tommasina, 519\n\n Transylvania, 203\n\n triangle, 58\n angle sum of, 58\n\n truth, 205\n\n Tycho Brahe, 133, 153, 228\n\n\n unity of nature, 130\n\n universal invariant, 333\n\n Uriel, 203\n\n\n van der Waals, 153\n\n Vauban, 210\n\n Veblen, 203\n\n velocity of light, 232, 312\n\n Venus of Milo, 201\n\n verification, 33\n\n Virchow, 21\n\n visual impressions, 252\n space, 67, 252\n\n Volga, 203\n\n Voltaire, 537-8\n\n\n Weber, 117, 515-6\n\n Weierstrass, 11, 212, 432\n\n Whitehead, 472, 481-2\n\n whole numbers, 44\n\n Wiechert, 145, 488\n\n\n x-rays, 152, 511, 520\n\n\n Zeeman effect, 152, 196, 317, 494\n\n Zeno, 382\n\n Zermelo, 477, 482-3\n\n zigzag theory, 478\n\n zodiac, 398, 404\n\n\n * * * * *\n\n\nTranscriber's Note: The Greek alphabets are represented within square\nbrackets. For example, [alpha] stands for first Greek alphabet alpha.\nSquare root of a number is represented using the symbol (sqrt). That\nis to say, sqrt(25) stands for square root of 25. The superscript is\nshown with carat (^) symbol, example, 10^{5} stands for 5th power of\n10. Similarly, subscript is represented by underscore (_) symbol. For\ninstance, n_{3} stands for letter n with subscript 3.","title":"The Foundations of Science: Science and Hypothesis, The Value of Science, Science and Method","tradition":"philosophy-ethics","translated_text":null,"word_count":198514}