{"collection":"philosophy-ethics","full_text_available":true,"graph_url":"https://unchartedknowledge.5gfusion.net/v2/api/page/gutenberg_57359/graph","html_url":"https://unchartedknowledge.5gfusion.net/v2/page/gutenberg_57359","id":"gutenberg_57359","license":"Public Domain (US)","rights_basis":"gutenberg_metadata_copyright_false","source":"gutenberg","source_url":"https://www.gutenberg.org/ebooks/57359","summary":null,"tags":["Category: Mathematics","Category: Philosophy & Ethics","Category: Research Methods/Statistics/Information Sys","Chance","Logic, Symbolic and mathematical","Mathematics","Probabilities","Science -- Methodology"],"text":"Produced by Juliet Sutherland, Andrew D. Hwang, and the\nOnline Distributed Proofreading Team at http://www.pgdp.net.\n\n\n\n\n\nTranscriber's Note\n\nMinor typographical errors and irregularities have been corrected.\n\nFootnotes have been numbered sequentially within chapters and moved\nto the end of each chapter.\n\n\n\n\nTHE\nLOGIC OF CHANCE\n\nAN ESSAY\n\nON THE FOUNDATIONS AND PROVINCE OF\nTHE THEORY OF PROBABILITY,\n\nWITH ESPECIAL REFERENCE TO ITS LOGICAL BEARINGS\nAND ITS APPLICATION TO\n\nMORAL AND SOCIAL SCIENCE AND TO STATISTICS,\n\n\nBY\n\nJOHN VENN, Sc.D., F.R.S.,\n\nFELLOW AND LECTURER IN THE MORAL SCIENCES, GONVILLE AND CAIUS COLLEGE,\nCAMBRIDGE.\n\nLATE EXAMINER IN LOGIC AND MORAL PHILOSOPHY IN THE\nUNIVERSITY OF LONDON.\n\n\n\"So careful of the type she seems\nSo careless of the single life.\"\n\n\n_THIRD EDITION, RE-WRITTEN AND ENLARGED._\n\n\nLondon:\nMACMILLAN AND CO.\nAND NEW YORK\n1888\n\n[_All Rights reserved._]\n\n\n\n\n_First Edition printed_ 1866.\n_Second Edition_ 1876.\n_Third Edition_ 1888.\n\n\n\n\nPREFACE TO FIRST EDITION\n\nAny work on Probability by a Cambridge man will be so\nlikely to have its scope and its general treatment of the\nsubject prejudged, that it may be well to state at the outset\nthat the following Essay is in no sense mathematical. Not\nonly, to quote a common but often delusive assurance, will\n'no knowledge of mathematics beyond the simple rules of\nArithmetic' be required to understand these pages, but it is\nnot intended that any such knowledge should be acquired by\nthe process of reading them. Of the two or three occasions\non which algebraical formul\u00e6 occur they will not be found to\nform any essential part of the text.\n\nThe science of Probability occupies at present a somewhat\nanomalous position. It is impossible, I think, not to\nobserve in it some of the marks and consequent disadvantages\nof a _sectional_ study. By a small body of ardent students it\nhas been cultivated with great assiduity, and the results they\nhave obtained will always be reckoned among the most extraordinary\nproducts of mathematical genius. But by the\ngeneral body of thinking men its principles seem to be\nregarded with indifference or suspicion. Such persons may\nadmire the ingenuity displayed, and be struck with the profundity\nof many of the calculations, but there seems to\nthem, if I may so express it, an _unreality_ about the whole\ntreatment of the subject. To many persons the mention of\nProbability suggests little else than the notion of a set of\nrules, very ingenious and profound rules no doubt, with which\nmathematicians amuse themselves by setting and solving\npuzzles.\n\nIt must be admitted that some ground has been given\nfor such an opinion. The examples commonly selected by\nwriters on the subject, though very well adapted to illustrate\nits rules, are for the most part of a special and peculiar\ncharacter, such as those relating to dice and cards. When\nthey have searched for illustrations drawn from the practical\nbusiness of life, they have very generally, but unfortunately,\nhit upon just the sort of instances which, as I shall endeavour\nto show hereafter, are among the very worst that could\nbe chosen for the purpose. It is scarcely possible for any\nunprejudiced person to read what has been written about the\ncredibility of witnesses by eminent writers, without his experiencing\nan invincible distrust of the principles which they\nadopt. To say that the rules of evidence sometimes given\nby such writers are broken in practice, would scarcely be\ncorrect; for the rules are of such a kind as generally to defy\nany attempt to appeal to them in practice.\n\nThis supposed want of harmony between Probability and\nother branches of Philosophy is perfectly erroneous. It\narises from the belief that Probability is a branch of mathematics\ntrying to intrude itself on to ground which does not\naltogether belong to it. I shall endeavour to show that this\nbelief is unfounded. To answer correctly the sort of questions\nto which the science introduces us does generally demand\nsome knowledge of mathematics, often a great knowledge,\nbut the discussion of the fundamental principles on which\nthe rules are based does not necessarily require any such\nqualification. Questions might arise in other sciences, in\nGeology, for example, which could only be answered by the\naid of arithmetical calculations. In such a case any one\nwould admit that the arithmetic was extraneous and accidental.\nHowever many questions of this kind there might\nbe here, those persons who do not care to work out special\nresults for themselves might still have an accurate knowledge\nof the principles of the science, and even considerable\nacquaintance with the details of it. The same holds true in\nProbability; its connection with mathematics, though certainly\nfar closer than that of most other sciences, is still of\nmuch the same kind. It is principally when we wish to\nwork out results for ourselves that mathematical knowledge\nis required; without such knowledge the student may still\nhave a firm grasp of the principles and even see his way to\nmany of the derivative results.\n\nThe opinion that Probability, instead of being a branch of\nthe general science of evidence which happens to make much\nuse of mathematics, _is_ a portion of mathematics, erroneous as\nit is, has yet been very disadvantageous to the science in\nseveral ways. Students of Philosophy in general have thence\nconceived a prejudice against Probability, which has for the\nmost part deterred them from examining it. As soon as a\nsubject comes to be considered 'mathematical' its claims\nseem generally, by the mass of readers, to be either on the\none hand scouted or at least courteously rejected, or on the\nother to be blindly accepted with all their assumed consequences.\nOf impartial and liberal criticism it obtains little\nor nothing.\n\nThe consequences of this state of things have been, I\nthink, disastrous to the students themselves of Probability.\nNo science can safely be abandoned entirely to its own devotees.\nIts details of course can only be studied by those who\nmake it their special occupation, but its general principles\nare sure to be cramped if it is not exposed occasionally to\nthe free criticism of those whose main culture has been of\na more general character. Probability has been very much\nabandoned to mathematicians, who as mathematicians have\ngenerally been unwilling to treat it thoroughly. They have\nworked out its results, it is true, with wonderful acuteness,\nand the greatest ingenuity has been shown in solving various\nproblems that arose, and deducing subordinate rules. And\nthis was all that they could in fairness be expected to do.\nAny subject which has been discussed by such men as\nLaplace and Poisson, and on which they have exhausted all\ntheir powers of analysis, could not fail to be profoundly\ntreated, so far as it fell within their province. But from this\nprovince the real principles of the science have generally\nbeen excluded, or so meagrely discussed that they had better\nhave been omitted altogether. Treating the subject as mathematicians\nsuch writers have naturally taken it up at the\npoint where their mathematics would best come into play,\nand that of course has not been at the foundations. In the\nworks of most writers upon the subject we should search in\nvain for anything like a critical discussion of the fundamental\nprinciples upon which its rules rest, the class of\nenquiries to which it is most properly applicable, or the\nrelation it bears to Logic and the general rules of inductive\nevidence.\n\nThis want of precision as to ultimate principles is perfectly\ncompatible here, as it is in the departments of Morals\nand Politics, with a general agreement on processes and\nresults. But it is, to say the least, unphilosophical, and\ndenotes a state of things in which positive error is always\nliable to arise whenever the process of controversy forces us\nto appeal to the foundations of the science.\n\nWith regard to the remarks in the last few paragraphs,\nprominent exceptions must be made in the case of two recent\nworks at least.[1] The first of these is Professor de Morgan's\n_Formal Logic_. He has there given an investigation into the\nfoundations of Probability as conceived by him, and nothing\ncan be more complete and precise than his statement of\nprinciples, and his deductions from them. If I could at all\nagree with these principles there would have been no necessity\nfor the following essay, as I could not hope to add\nanything to their foundation, and should be far indeed from\nrivalling his lucid statement of them. But in his scheme\nProbability is regarded very much from the Conceptualist\npoint of view; as stated in the preface, he considers that\nProbability is concerned with formal inferences in which the\npremises are entertained with a conviction short of absolute\ncertainty. With this view I cannot agree. As I have entered\ninto criticism of some points of his scheme in one of the\nfollowing chapters, and shall have occasion frequently to refer\nto his work, I need say no more about it here. The other\nwork to which I refer is the profound _Laws of Thought_ of\nthe late Professor Boole, to which somewhat similar remarks\nmay in part be applied. Owing however to his peculiar\ntreatment of the subject, I have scarcely anywhere come\ninto contact with any of his expressed opinions.\n\nThe view of the province of Probability adopted in this\nEssay differs so radically from that of most other writers on\nthe subject, and especially from that of those just referred to,\nthat I have thought it better, as regards details, to avoid all\ncriticism of the opinions of others, except where conflict was\nunavoidable. With regard to that radical difference itself\nBacon's remark applies, behind which I must shelter myself\nfrom any change of presumption.--\"Quod ad universalem\nistam reprehensionem attinet, certissimum vere est rem reputanti,\neam et magis probabilem esse et magis modestam,\nquam si facta fuisset ex parte.\"\n\nAlmost the only writer who seems to me to have expressed\na just view of the nature and foundation of the rules\nof Probability is Mr Mill, in his _System of Logic_.[2] His\ntreatment of the subject is however very brief, and a considerable\nportion of the space which he has devoted to it is\noccupied by the discussion of one or two special examples.\nThere are moreover some errors, as it seems to me, in what\nhe has written, which will be referred to in some of the\nfollowing chapters.\n\nThe reference to the work just mentioned will serve to\nconvey a general idea of the view of Probability adopted in\nthis Essay. With what may be called the Material view of\nLogic as opposed to the Formal or Conceptualist,--with that\nwhich regards it as taking cognisance of laws of things and\nnot of the laws of our own minds in thinking about things,--I\nam in entire accordance. Of the province of Logic, regarded\nfrom this point of view, and under its widest aspect, Probability\nmay, in my opinion, be considered to be a portion. The\nprincipal objects of this Essay are to ascertain how great a\nportion it comprises, where we are to draw the boundary between\nit and the contiguous branches of the general science\nof evidence, what are the ultimate foundations upon which its\nrules rest, what the nature of the evidence they are capable\nof affording, and to what class of subjects they may most fitly\nbe applied. That the science of Probability, on this view of\nit, contains something more important than the results of a\nsystem of mathematical assumptions, is obvious. I am convinced\nmoreover that it can and ought to be rendered both\ninteresting and intelligible to ordinary readers who have any\ntaste for philosophy. In other words, if the large and growing\nbody of readers who can find pleasure in the study of\nbooks like Mill's _Logic_ and Whewell's _Inductive Sciences_,\nturn with aversion from a work on Probability, the cause in\nthe latter case must lie either in the view of the subject or\nin the manner and style of the book.\n\nI take this opportunity of thanking several friends,\namongst whom I must especially mention Mr Todhunter, of\nSt John's College, and Mr H. Sidgwick, of Trinity College,\nfor the trouble they have kindly taken in looking over the\nproof-sheets, whilst this work was passing through the Press.\nTo the former in particular my thanks are due for thus\nadding to the obligations which I, as an old pupil, already\nowed him, by taking an amount of trouble, in making suggestions\nand corrections for the benefit of another, which few\nwould care to take for anything but a work of their own.\nHis extensive knowledge of the subject, and his extremely\naccurate judgment, render the service he has thus afforded\nme of the greatest possible value.\n\nGONVILLE AND CAIUS COLLEGE\n_September_ 1866.\n\n\n1. I am here speaking, of course, of\n  those only who have expressly treated\n  of the foundations of the science. Mr\n  Todhunter's admirable work on the\n  _History of the Theory of Probability_\n  being, as the name denotes, mainly\n  historical, such enquiries have not\n  directly fallen within his province.\n\n2. This remark, and that at the\n  commencement of the last paragraph,\n  having been misunderstood, I ought\n  to say that the only sense in which\n  originality is claimed for this Essay\n  is in the thorough working out of the\n  Material view of Logic as applied to\n  Probability. I have given a pretty\n  full discussion of the general principles\n  of this view in the tenth\n  chapter, and have there pointed out\n  some of the peculiarities to which it\n  leads.\n\n\n\n\nPREFACE TO SECOND EDITION\n\nThe principal reason for designating this volume a second\nedition consists in the fact that the greater portion of what\nmay be termed the first edition is incorporated into it. Besides\nvarious omissions (principally where the former treatment\nhas since seemed to me needlessly prolix), I have added\nnew matter, not much inferior in amount to the whole of\nthe original work. In addition, moreover, to these alterations\nin the matter, the general arrangement of the subject\nas regards the successive chapters has been completely\nchanged; the former arrangement having been (as it now\nseems to me) justly objected to as deficient and awkward in\nmethod.\n\nAfter saying this, it ought to be explained whether any\nchange of general view or results will be found in the present\ntreatment.\n\nThe general view of Probability adopted is quite unchanged,\nfurther reading and reflection having only confirmed\nme in the conviction that this is the soundest and most\nfruitful way of regarding the subject. It is the more necessary\nto say this, as to a cursory reader it might seem\notherwise; owing to my having endeavoured to avoid the\nneedlessly polemical tone which, as is often the case with\nthose who are making their first essay in writing upon any\nsubject, was doubtless too prominent in the former edition.\nI have not thought it necessary, of course, except in one or\ntwo cases, to indicate points of detail which it has seemed\nnecessary to correct.\n\nA number of new discussions have been introduced upon\ntopics which were but little or not at all treated before. The\nprincipal of these refer to the nature and physical origin of\nLaws of Error (Ch. II.); the general view of Logic, and consequently\nof Probability, termed the Material view, adopted\nhere (Ch. X.); a brief history and criticism of the various\nopinions held on the subject of Modality (Ch. XII.); the\nlogical principles underlying the method of Least Squares\n(Ch. XIII.); and the practices of Insurance and Gambling,\nso far as the principles involved in them are concerned\n(Ch. XV.). The Chapter on the Credibility of Extraordinary\nStories is also mainly new; this was the portion of the former\nwork which has since seemed to me the least satisfactory,\nbut owing to the extreme intricacy of the subject I am far\nfrom feeling thoroughly satisfied with it even now.\n\nI have again to thank several friends for the assistance\nthey have so kindly afforded. Amongst these I must prominently\nmention Mr C. J. Monro, late fellow of Trinity. It is\nonly the truth to say that I have derived more assistance from\nhis suggestions and criticisms than has been consciously obtained\nfrom all other external sources together. Much of this\ncriticism has been given privately in letters, and notes on\nthe proof-sheets; but one of the most elaborate of his discussions\nof the subject was communicated to the Cambridge\nPhilosophical Society some years ago; as it was not published,\nhowever, I am unfortunately unable to refer the reader to it.\nI ought to add that he is not in any way committed to any\nof my opinions upon the subject, from some of which in fact\nhe more or less dissents. I am also much indebted to\nMr J. W. L. Glaisher, also of Trinity College, for many hints\nand references to various publications upon the subject of\nLeast Squares, and for careful criticism (given in the midst\nof much other labour) of the chapter in which that subject is\ntreated.\n\nI need not add that, like every one else who has had to\ndiscuss the subject of Probability during the last ten years,\nI have made constant use of Mr Todhunter's History.\n\nI may take this opportunity of adding that a considerable\nportion of the tenth chapter has recently appeared in the\nJanuary number of _Mind_, and that the substance of several\nchapters, especially in the more logical parts, has formed part\nof my ordinary lectures in Cambridge; the foundation and\nlogical treatment of Probability being now expressly included\nin the Schedule of Subjects for the Moral Sciences Tripos.\n\n_March_ 1876.\n\n\n\n\nPREFACE TO THIRD EDITION\n\nThe present edition has been revised throughout, and in fact\nrewritten. Three chapters are new, viz. the fifth (On the\nconception of Randomness) and the eighteenth and nineteenth\n(On the nature, and on the employment, of Averages).\nThe eighth, tenth, eleventh, and fifteenth chapters have been\nrecast, and much new matter added, and numerous alterations\nmade in the remaining portions.[1] On the other hand\nthree chapters of the last edition have been nearly or\nentirely omitted.\n\nThese alterations do not imply any appreciable change of\nview on my part as to the foundations and province of\nProbability. Some of them are of course due to the necessary\nchanges involved in the attempt to write up to date upon a\nsubject which has not been stationary during the last eleven\nyears. For instance the greatly increased interest now\ntaken in what may be called the Theory of Statistics has\nrendered it desirable to go much more fully into the Nature\nand treatment of Laws of Error. The omissions are mainly\ndue to a wish to avoid increasing the bulk of this volume\nmore than is actually necessary, and to a feeling that the\nportions treating specially of Inductive Logic (which occupied\nsome space in the last edition) would be more\nsuitable to a regular work on that subject. I am at present\nengaged on such a work.\n\nThe publications which I have had occasion to notice\nhave mostly appeared in various scientific journals. The\nprincipal authors of these have been Mr F. Galton and\nMr F. Y. Edgeworth: to the latter of whom I am also\npersonally much obliged for many discussions, oral and\nwritten, and for his kindness in looking through the proof-sheets.\nHis published articles are too numerous for separate\nmention here, but I may say generally, in addition to the\nobligations specially noticed, that I have been considerably\nindebted to them in writing the last two chapters. Two\nauthors of works of a somewhat more substantial character,\nviz. Prof. Lexis and Von Kries, only came under my notice\nunfortunately after this work was already in the printer's\nhands. With the latter of these authors I find myself in\ncloser agreement than with most others, in respect of his\ngeneral conception and treatment of Probability.\n\n_December_ 1887.\n\n\n1. I have indicated the new chapters and sections by printing them in\n  italics in the Table of Contents.\n\n\n\n\nTABLE OF CONTENTS.[1]\n\n1. Chapters and sections which are nearly or entirely new are printed\nin _italics_.\n\n\nPART I.\n\nPHYSICAL FOUNDATIONS OF THE SCIENCE OF PROBABILITY. Chh. I-V.\n\n\nCHAPTER I.\n\nTHE SERIES OF PROBABILITY.\n\n\u00a7\u00a7 1, 2. Distinction between the proportional propositions of Probability,\n       and the propositions of Logic.\n   3, 4. The former are best regarded as presenting a series of individuals,\n   5. Which may occur in any order of time,\n   6, 7. And which present themselves in groups.\n   8. Comparison of the above with the ordinary phraseology.\n   9, 10. These series ultimately fluctuate,\n   11. Especially in the case of moral and social phenomena,\n   12. Though in the case of games of chance the fluctuation is practically\n       inappreciable.\n   13, 14. In this latter case only can rigorous inferences be drawn.\n   15, 16. The Petersburg Problem.\n\n\nCHAPTER II.\n\nARRANGEMENT AND FORMATION OF THE SERIES. LAWS OF ERROR.\n\n\u00a7\u00a7 1, 2. Indication of the nature of a Law of Error or Divergence.\n   3. Is there necessarily but one such law,\n   4. Applicable to widely distinct classes of things?\n   5, 6. This cannot be proved directly by statistics;\n   7, 8. _Which in certain cases show actual asymmetry._\n   9, 10. Nor deductively;\n   11. Nor by the Method of Least Squares.\n   12. Distinction between Laws of Error and the Method of Least\n       Squares.\n   13. Supposed existence of types.\n   14-16. Homogeneous and heterogeneous classes.\n   17, 18. _The type in the case of human stature, &c._\n   19, 20. The type in mental characteristics.\n   21, 22. Applications of the foregoing principles and results.\n\n\nCHAPTER III.\n\nORIGIN OR PROCESS OF CAUSATION OF THE SERIES.\n\n\u00a7  1. The causes consist of (1) 'objects,'\n   2, 3. Which may or may not be distinguishable into natural kinds,\n   4-6. And (2) 'agencies.'\n   7. Requisites demanded in the above:\n   8, 9. Consequences of their absence.\n   10. Where are the required causes found?\n   11, 12. Not in the direct results of human will.\n   13-15. Examination of apparent exceptions.\n   16-18. _Further analysis of some natural causes._\n\n\nCHAPTER IV.\n\nHOW TO DISCOVER AND PROVE THE SERIES.\n\n\u00a7  1. The data of Probability are established by experience;\n   2. Though in practice most problems are solved deductively.\n   3-7. Mechanical instance to show the inadequacy of any \u00e0 priori proof.\n   8. The Principle of Sufficient Reason inapplicable.\n   9. Evidence of actual experience.\n   10, 11. Further examination of the causes.\n   12, 13. Distinction between the succession of physical events and the\n       Doctrine of Combinations.\n   14, 15. Remarks of Laplace on this subject.\n   16. Bernoulli's Theorem;\n   17, 18. Its inapplicability to social phenomena.\n   19. Summation of preceding results.\n\n\nCHAPTER V.\n\nTHE CONCEPTION OF RANDOMNESS.\n\n\u00a7  1. _General Indication._\n   2-5. _The postulate of ultimate uniform distribution at one stage or\n       another._\n   6. _This area of distribution must be finite:_\n   7, 8. _Geometrical illustrations in support:_\n   9. _Can we conceive any exception here?_\n   10, 11. _Experimental determination of the random character when the\n       events are many:_\n   12. _Corresponding determination when they are few._\n   13, 14. _Illustration from the constant \u03c0._\n   15, 16. _Conception of a line drawn at random._\n   17. _Graphical illustration._\n\n\nPART II.\n\nLOGICAL SUPERSTRUCTURE ON THE ABOVE PHYSICAL FOUNDATIONS.\nChh. VI-XIV.\n\n\nCHAPTER VI.\n\nMEASUREMENT OF BELIEF.\n\n\u00a7\u00a7 1, 2. Preliminary remarks.\n   3, 4. Are we accurately conscious of gradations of belief?\n   5. Probability only concerned with part of this enquiry.\n   6. Difficulty of measuring our belief;\n   7. Owing to intrusion of emotions,\n   8. And complexity of the evidence.\n   9. And when measured, is it always correct?\n   10, 11. Distinction between logical and psychological views.\n   12-16. Analogy of Formal Logic fails to show that we can thus detach\n       and measure our belief.\n   17. Apparent evidence of popular language to the contrary.\n   18. How is full belief justified in inductive enquiry?\n   19-23. Attempt to show how partial belief may be similarly justified.\n   24-28. Extension of this explanation to cases which cannot be repeated\n       in experience.\n   29. Can other emotions besides belief be thus measured?\n   30. Errors thus arising in connection with the Petersburg Problem.\n   31, 32. The emotion of surprise is a partial exception.\n   33, 34. Objective and subjective phraseology.\n   35. The definition of probability,\n   36. Introduces the notion of a 'limit',\n   37. And implies, vaguely, some degree of belief.\n\n\nCHAPTER VII.\n\nTHE RULES OF INFERENCE IN PROBABILITY.\n\n\u00a7  1. Nature of these inferences.\n   2. Inferences by addition and subtraction.\n   3. Inferences by multiplication and division.\n   4-6. Rule for independent events.\n   7. Other rules sometimes introduced.\n   8. All the above rules may be interpreted subjectively, i.e. in terms\n       of belief.\n   9-11. Rules of so-called Inverse Probability.\n   12, 13. Nature of the assumption involved in them:\n   14-16. Arbitrary character of this assumption.\n   17, 18. _Physical illustrations._\n\n\nCHAPTER VIII.\n\nTHE RULE OF SUCCESSION.\n\n\u00a7  1. Reasons for desiring some such rule:\n   2. Though it could scarcely belong to Probability.\n   3. Distinction between Probability and Induction.\n   4, 5. Impossibility of reducing the various rules of the latter under\n       one head.\n   6. Statement of the Rule of Succession;\n   7. _Proof offered for it._\n   8. _Is it a strict rule of inference?_\n   9. _Or is it a psychological principle?_\n\n\nCHAPTER IX.\n\nINDUCTION.\n\n\u00a7\u00a7 1-5. Statement of the Inductive problem, and origin of the Inductive\ninference.\n   6. Relation of Probability to Induction.\n   7-9. The two are sometimes merged into one.\n   10. Extent to which causation is needed in Probability.\n   11-13. Difficulty of referring an individual to a class:\n   14. This difficulty but slight in Logic,\n   15, 16. But leads to perplexity in Probability:\n   17-21. Mild form of this perplexity;\n   22, 23. Serious form.\n   24-27. Illustration from Life Insurance.\n   28, 29. Meaning of 'the value of a life'.\n   30, 31. Successive specialization of the classes to which objects are\n       referred.\n   32. Summary of results.\n\n\nCHAPTER X.\n\nCHANGE, CAUSATION AND DESIGN.\n\n\u00a7  1. Old Theological objection to Chance.\n   2-4. Scientific version of the same.\n   5. Statistics in reference to Free-will.\n   6-8. Inconclusiveness of the common arguments here.\n   9, 10. _Chance as opposed to Physical Causation._\n   11. _Chance as opposed to Design in the case of numerical constants._\n   12-14. _Theoretic solution between Chance and Design._\n   15. _Illustration from the dimensions of the Pyramid._\n   16, 17. _Discussion of certain difficulties here._\n   18, 19. _Illustration from Psychical Phenomena._\n   20. Arbuthnott's Problem of the proportion of the sexes.\n   21-23. Random or designed distribution of the stars.\n\n(_Note on the proportion of the sexes_.)\n\n\nCHAPTER XI.\n\nMATERIAL AND FORMAL LOGIC.\n\n\u00a7\u00a7 1, 2. _Broad distinction between these views;_\n   2, 3. _Difficulty of adhering consistently to the objective view;_\n   4. _Especially in the case of Hypotheses._\n   5. The doubtful stage of our facts is only occasional in Inductive\n       Logic.\n   6-9. But normal and permanent in Probability.\n   10, 11. Consequent difficulty of avoiding Conceptualist phraseology.\n\n\nCHAPTER XII.\n\nCONSEQUENCES OF THE DISTINCTIONS OF THE PREVIOUS CHAPTER.\n\n\u00a7\u00a7 1, 2. Probability has no relation to time.\n   3, 4. Butler and Mill on Probability before and after the event.\n   5. Other attempts at explaining the difficulty.\n   6-8. What is really meant by the distinction.\n   9. Origin of the common mistake.\n   10-12. Examples in illustration of this view,\n   13. Is Probability relative?\n   14. What is really meant by this expression.\n   15. Objections to terming Probability relative.\n   16, 17. In suitable examples the difficulty scarcely presents itself.\n\n\nCHAPTER XIII.\n\nON MODALITY.\n\n\u00a7  1. Various senses of Modality;\n   2. Having mostly some relation to Probability.\n   3. Modality must be recognized.\n   4. Sometimes relegated to the predicate,\n   5, 6. Sometimes incorrectly rejected altogether.\n   7, 8. Common practical recognition of it.\n   9-11. Modal propositions in Logic and in Probability.\n   12. Aristotelian view of the Modals;\n   13, 14. Founded on extinct philosophical views;\n   15. But long and widely maintained.\n   16. Kant's general view.\n   17-19. The number of modal divisions admitted by various logicians.\n   20. Influence of the theory of Probability.\n   21, 22. Modal syllogisms.\n   23. Popular modal phraseology.\n   24-26. Probable and Dialectic syllogisms.\n   27, 28. Modal difficulties occur in Jurisprudence.\n   29, 30. Proposed standards of legal certainty.\n   31. Rejected formally in English Law, but possibly recognized practically.\n   32. How, if so, it might be determined.\n\n\nCHAPTER XIV.\nFALLACIES.\n\n\u00a7\u00a7 1-3. (I.) Errors in judging of events after they have happened.\n   4-7. Very various judgments may be thus involved.\n   8, 9. (II.) _Confusion between random and picked selections._\n   10, 11. (III.) Undue limitation of the notion of Probability.\n   12-16. (IV.) Double or Quits: the Martingale.\n   17, 18. Physical illustration.\n   19, 20. (V.) Inadequate realization of large numbers.\n   21-24. Production of works of art by chance.\n   25. Illustration from doctrine of heredity.\n   26-30. (VI.) Confusion between Probability and Induction.\n   31-33. (VII.) Undue neglect of small chances.\n   34, 35. (VIII.) _Judging by the event in Probability and in Induction._\n\n\nPART III.\n\nVARIOUS APPLICATIONS OF THE THEORY OF PROBABILITY. Chh. XV-XIX.\n\n\nCHAPTER XV.\n\nINSURANCE AND GAMBLING.\n\n\u00a7\u00a7 1, 2. The certainties and uncertainties of life.\n   3-5. Insurance a means of diminishing the uncertainties.\n   6, 7. Gambling a means of increasing them.\n   8, 9. Various forms of gambling.\n   10, 11. _Comparison between these practices._\n   12-14. Proofs of the disadvantage of gambling:--\n       (1) on arithmetical grounds:\n   15, 16. _Illustration from family names._\n   17. (2) from the 'moral expectation'.\n   18, 19. _Inconclusiveness of these proofs._\n   20-22. _Broader questions raised by these attempts._\n\n\nCHAPTER XVI.\n\nAPPLICATION OF PROBABILITY TO TESTIMONY.\n\n\u00a7\u00a7 1, 2. Doubtful applicability of Probability to testimony.\n   3. Conditions of such applicability.\n   4. Reasons for the above conditions.\n   5, 6. Are these conditions fulfilled in the case of testimony?\n   7. The appeal here is not directly to statistics.\n   8, 9. Illustrations of the above.\n   10, 11. Is any application of Probability to testimony valid?\n\n\nCHAPTER XVII.\n\nCREDIBILITY OF EXTRAORDINARY STORIES.\n\n\u00a7  1. Improbability before and after the event.\n   2, 3. Does the rejection of this lead to the conclusion that the\n      credibility of a story is independent of its nature?\n   4. General and special credibility of a witness.\n   5-8. Distinction between alternative and open questions, and the\n       usual rules for application of testimony to each of these.\n   9. _Discussion of an objection._\n   10, 11. Testimony of worthless witnesses.\n   12-14. Common practical ways of regarding such problems.\n   15. Extraordinary stories not necessarily less probable.\n   16-18. Meaning of the term extraordinary, and its distinction from\n       miraculous.\n   19, 20. Combination of testimony.\n   21, 22. Scientific meaning of a miracle.\n   23, 24. Two distinct prepossessions in regard to miracles, and the\n       logical consequences of these.\n   25. Difficulty of discussing by our rules cases in which arbitrary\n       interference can be postulated.\n   26, 27. Consequent inappropriateness of many arguments.\n\n\nCHAPTER XVIII.\n\nON THE NATURE AND USE OF AN AVERAGE, AND ON THE DIFFERENT KINDS OF AVERAGE.\n\n\u00a7  1. _Preliminary rude notion of an average,_\n   2. _More precise quantitative notion, yielding_\n      (1) _the Arithmetical Average,_\n   3. (2) _the Geometrical._\n   4. _In asymmetrical curves of error the arithmetic average must be\n       distinguished from,_\n   5. (3) _the Maximum Ordinate average,_\n   6. (4) _and the Median._\n   7. _Diagram in illustration._\n   8-10. _Average departure from the average, considered under the above\n       heads, and under that of_\n   11. (5) _The (average of) Mean Square of Error,_\n   12-14. _The objects of taking averages._\n   15. _Mr Galton's practical method of determining the average._\n   16, 17. _No distinction between the average and the mean._\n   18-20. _Distinction between what is necessary and what is experimental\n       here._\n   21, 22. _Theoretical defects in the determination of the 'errors'._\n   23. _Practical escape from these._\n\n(_Note about the units in the exponential equation and integral._)\n\n\nCHAPTER XIX.\n\nTHE THEORY OF THE AVERAGE AS A MEANS OF APPROXIMATION TO THE TRUTH.\n\n\u00a7\u00a7 1-4. _General indication of the problem: i.e. an inverse one\n    requiring the previous consideration of a direct one._\n\n    [I. _The direct problem:--given the central value and law of\n    dispersion of the single errors, to determine those of the\n    averages._ \u00a7\u00a7 6-20.]\n\n   6. (i) _The law of dispersion may be determinable _\u00e0 priori_,_\n   7. (ii) _or experimentally, by statistics._\n   8, 9. _Thence to determine the modulus of the error curve._\n   10-14. _Numerical example to illustrate the nature and amount of\n       the contraction of the modulus of the average-error curve._\n   15. _This curve is of the same general kind as that of the single errors;_\n   16. _Equally symmetrical,_\n   17, 18. _And more heaped up towards the centre._\n   19, 20. _Algebraic generalization of the foregoing results._\n\n    [II. _The inverse problem:--given but a few of the errors to\n    determine their centre and law, and thence to draw the above\n    deductions._ \u00a7\u00a7 21-25.]\n\n   22, 23. _The actual calculations are the same as before,_\n   24. _With the extra demand that we must determine how probable are the\n       results._\n   25. _Summary._\n\n    [III. _Consideration of the same questions as applied to certain\n    peculiar laws of error._ \u00a7\u00a7 26-37.]\n\n   26. (i) _All errors equally probable._\n   27, 28. (ii) _Certain peculiar laws of error._\n   29, 30. _Further analysis of the reasons for taking averages._\n   31-35. _Illustrative examples._\n   36, 37. _Curves with double centre and absence of symmetry._\n   38, 39. _Conclusion._\n\n\n\n\nTHE LOGIC OF CHANCE.\n\n\n\n\nCHAPTER I.\n\n\n_ON CERTAIN KINDS OF GROUPS OR SERIES AS THE FOUNDATION OF PROBABILITY._\n\n1. It is sometimes not easy to give a clear definition of a\nscience at the outset, so as to set its scope and province before\nthe reader in a few words. In the case of those sciences\nwhich are more immediately and directly concerned with\nwhat are termed objects, rather than with what are termed\nprocesses, this difficulty is not indeed so serious. If the\nreader is already familiar with the objects, a simple reference\nto them will give him a tolerably accurate idea of the\ndirection and nature of his studies. Even if he be not\nfamiliar with them, they will still be often to some extent\nconnected and associated in his mind by a name, and\nthe mere utterance of the name may thus convey a fair\namount of preliminary information. This is more or less\nthe case with many of the natural sciences; we can often\ntell the reader beforehand exactly what he is going to study.\nBut when a science is concerned, not so much with objects\ndirectly, as with processes and laws, or when it takes for the\nsubject of its enquiry some comparatively obscure feature\ndrawn from phenomena which have little or nothing else in\ncommon, the difficulty of giving preliminary information\nbecomes greater. Recognized classes of objects have then\nto be disregarded and even broken up, and an entirely novel\narrangement of the objects to be made. In such cases it is\nthe study of the science that first gives the science its unity,\nfor till it is studied the objects with which it is concerned\nwere probably never thought of together. Here a definition\ncannot be given at the outset, and the process of obtaining it\nmay become by comparison somewhat laborious.\n\nThe science of Probability, at least on the view taken of\nit in the following pages, is of this latter description. The\nreader who is at present unacquainted with the science\ncannot be at once informed of its scope by a reference to\nobjects with which he is already familiar. He will have\nto be taken in hand, as it were, and some little time\nand trouble will have to be expended in directing his\nattention to our subject-matter before he can be expected to\nknow it. To do this will be our first task.\n\n2. In studying Nature, in any form, we are continually\ncoming into possession of information which we sum up in\ngeneral propositions. Now in very many cases these general\npropositions are neither more nor less certain and accurate\nthan the details which they embrace and of which they are\ncomposed. We are assuming at present that the truth of\nthese generalizations is not disputed; as a matter of fact\nthey may rest on weak evidence, or they may be uncertain\nfrom their being widely extended by induction; what is\nmeant is, that when we resolve them into their component\nparts we have precisely the same assurance of the truth of\nthe details as we have of that of the whole. When I know,\nfor instance, that all cows ruminate, I feel just as certain\nthat any particular cow or cows ruminate as that the whole\nclass does. I may be right or wrong in my original statement,\nand I may have obtained it by any conceivable mode\nin which truths can be obtained; but whatever the value of\nthe general proposition may be, that of the particulars is\nneither greater nor less. The process of inferring the particular\nfrom the general is not accompanied by the slightest\ndiminution of certainty. If one of these 'immediate inferences'\nis justified at all, it will be equally right in every\ncase.\n\nBut it is by no means necessary that this characteristic\nshould exist in all cases. There is a class of immediate inferences,\nalmost unrecognized indeed in logic, but constantly\ndrawn in practice, of which the characteristic is, that as they\nincrease in particularity they diminish in certainty. Let me\nassume that I am told that _some_ cows ruminate; I cannot\ninfer logically from this that any particular cow does so,\nthough I should feel some way removed from absolute disbelief,\nor even indifference to assent, upon the subject; but\nif I saw a herd of cows I should feel more sure that some of\nthem were ruminant than I did of the single cow, and my\nassurance would increase with the numbers of the herd about\nwhich I had to form an opinion. Here then we have a class\nof things as to the individuals of which we feel quite in\nuncertainty, whilst as we embrace larger numbers in our\nassertions we attach greater weight to our inferences. It is\nwith such classes of things and such inferences that the\nscience of Probability is concerned.\n\n3. In the foregoing remarks, which are intended to\nbe purely preliminary, we have not been able altogether to\navoid some reference to a subjective element, viz. the degree\nof our certainty or belief about the things which we are\nsupposed to contemplate. The reader may be aware that\nby some writers this element is regarded as the subject-matter\nof the science. Hence it will have to be discussed\nin a future chapter. As however I do not agree with the\nopinion of the writers just mentioned, at least as regards\ntreating this element as one of primary importance, no\nfurther allusion will be made to it here, but we will pass on\nat once to a more minute investigation of that distinctive\ncharacteristic of certain classes of things which was introduced\nto notice in the last section.\n\nIn these classes of things, which are those with which\nProbability is concerned, the fundamental conception which\nthe reader has to fix in his mind as clearly as possible, is, I\ntake it, that of a series. But it is a series of a peculiar kind,\none of which no better compendious description can be given\nthan that which is contained in the statement that it combines\nindividual irregularity with aggregate regularity. This\nis a statement which will probably need some explanation.\nLet us recur to an example of the kind already alluded to,\nselecting one which shall be in accordance with experience.\nSome children will not live to thirty. Now if this proposition\nis to be regarded as a purely indefinite or, as it would\nbe termed in logic, 'particular' proposition, no doubt the\nnotion of a series does not obviously present itself in connection\nwith it. It contains a statement about a certain\nunknown proportion of the whole, and that is all. But it is\nnot with these purely indefinite propositions that we shall\nbe concerned. Let us suppose the statement, on the contrary,\nto be of a numerical character, and to refer to a given\nproportion of the whole, and we shall then find it difficult to\nexclude the notion of a series. We shall find it, I think,\nimpossible to do so as soon as we set before us the aim of\nobtaining accurate, or even moderately correct inferences.\nWhat, for instance, is the meaning of the statement that\ntwo new-born children in three fail to attain the age of\nsixty-three? It certainly does not declare that in any given\nbatch of, say, thirty, we shall find just twenty that fail:\nwhatever might be the strict meaning of the words, this\nis not the import of the statement. It rather contemplates\nour examination of a large number, of a long succession\nof instances, and states that in such a succession we shall\nfind a numerical proportion, not indeed fixed and accurate at\nfirst, but which tends in the long run to become so. In\nevery kind of example with which we shall be concerned we\nshall find this reference to a large number or succession\nof objects, or, as we shall term it, _series_ of them.\n\nA few additional examples may serve to make this plain.\n\nLet us suppose that we toss up a penny a great many\ntimes; the results of the successive throws may be conceived\nto form a series. The separate throws of this series seem to\noccur in utter disorder; it is this disorder which causes our\nuncertainty about them. Sometimes head comes, sometimes\ntail comes; sometimes there is a repetition of the same face,\nsometimes not. So long as we confine our observation to a\nfew throws at a time, the series seems to be simply chaotic.\nBut when we consider the result of a long succession we find\na marked distinction; a kind of order begins gradually to\nemerge, and at last assumes a distinct and striking aspect.\nWe find in this case that the heads and tails occur in about\nequal numbers, that similar repetitions of different faces do\nso also, and so on. In a word, notwithstanding the individual\ndisorder, an aggregate order begins to prevail. So again if\nwe are examining the length of human life, the different lives\nwhich fall under our notice compose a series presenting the\nsame features. The length of a single life is familiarly uncertain,\nbut the average duration of a batch of lives is becoming\nin an almost equal degree familiarly certain. The\nlarger the number we take out of any mixed crowd, the\nclearer become the symptoms of order, the more nearly will\nthe average length of each selected class be the same.\nThese few cases will serve as simple examples of a property\nof things which can be traced almost everywhere, to a\ngreater or less extent, throughout the whole field of our experience.\nFires, shipwrecks, yields of harvest, births, marriages,\nsuicides; it scarcely seems to matter what feature we\nsingle out for observation.[1] The irregularity of the single\ninstances diminishes when we take a large number, and at\nlast seems for all practical purposes to disappear.\n\nIn speaking of the effect of the average in thus diminishing\nthe irregularities which present themselves in the details,\nthe attention of the student must be prominently directed to\nthe point, that it is not the _absolute_ but the _relative_ irregularities\nwhich thus tend to diminish without limit. This\nidea will be familiar enough to the mathematician, but to\nothers it may require some reflection in order to grasp it\nclearly. The absolute divergences and irregularities, so far\nfrom diminishing, show a disposition to increase, and this (it\nmay be) without limit, though their relative importance shows\na corresponding disposition to diminish without limit. Thus\nin the case of tossing a penny, if we take a few throws, say\nten, it is decidedly unlikely that there should be a difference\nof six between the numbers of heads and tails; that is, that\nthere should be as many as eight heads and therefore as few\nas two tails, or _vice vers\u00e2_. But take a thousand throws, and\nit becomes in turn exceedingly likely that there should be\nas much as, or more than, a difference of six between the\nrespective numbers. On the other hand the _proportion_ of\nheads to tails in the case of the thousand throws will be very\nmuch nearer to unity, in most cases, than when we only took\nten. In other words, the longer a game of chance continues\nthe larger are the spells and runs of luck in themselves, but\nthe less their relative proportions to the whole amounts\ninvolved.\n\n4. In speaking as above of events or things as to the\ndetails of which we know little or nothing, it is not of course\nimplied that our ignorance about them is complete and universal,\nor, what comes to the same thing, that irregularity\nmay be observed in all their qualities. All that is meant is\nthat there are _some_ qualities or marks in them, the existence\nof which we are not able to predicate with certainty in the\nindividuals. With regard to all their other qualities there\nmay be the utmost uniformity, and consequently the most\ncomplete certainty. The irregularity in the length of human\nlife is notorious, but no one doubts the existence of such\norgans as a heart and brains in any person whom he happens\nto meet. And even in the qualities in which the irregularity\nis observed, there are often, indeed generally, positive limits\nwithin which it will be found to be confined. No person,\nfor instance, can calculate what may be the length of any\nparticular life, but we feel perfectly certain that it will not\nstretch out to 150 years. The irregularity of the individual\ninstances is only shown in certain respects, as e.g. the length\nof the life, and even in these respects it has its limits. The\nsame remark will apply to most of the other examples with\nwhich we shall be concerned. The disorder in fact is not\nuniversal and unlimited, it only prevails in certain directions\nand up to certain points.\n\n5. In speaking as above of a series, it will hardly be\nnecessary to point out that we do not imply that the objects\nthemselves which compose the series must occur successively\nin time; the series may be formed simply by their coming\nin succession under our notice, which as a matter of fact\nthey may do in any order whatever. A register of mortality,\nfor instance, may be made up of deaths which took place\nsimultaneously or successively; or, we might if we pleased\narrange the deaths in an order quite distinct from either of\nthese. This is entirely a matter of indifference; in all these\ncases the series, for any purposes which we need take into\naccount, may be regarded as being of precisely the same description.\nThe objects, be it remembered, are given to us in\nnature; the order under which we view them is our own private\narrangement. This is mentioned here simply by way of\ncaution, the meaning of this assertion will become more plain\nin the sequel.\n\nI am aware that the word 'series' in the application with\nwhich it is used here is liable to some misconstruction, but I\ncannot find any better word, or indeed any as suitable in all\nrespects. As remarked above, the events need not necessarily\nhave occurred in a regular sequence of time, though\nthey often will have done so. In many cases (for instance,\nthe throws of a penny or a die) they really do occur in succession;\nin other cases (for instance, the heights of men, or\nthe duration of their lives), whatever may have been the\norder of their actual occurrence, they are commonly brought\nunder our notice in succession by being arranged in statistical\ntables. In all cases alike our processes of inference involve\nthe necessity of examining one after another of the members\nwhich compose the group, or at least of being prepared to do\nthis, if we are to be in a position to justify our inferences.\nThe force of these considerations will come out in the course\nof the investigation in Chapter VI.\n\nThe late Leslie Ellis[2] has expressed what seems to me\na substantially similar view in terms of genus and species,\ninstead of speaking of a series. He says, \"When individual\ncases are considered, we have no conviction that the ratios of\nfrequency of occurrence depend on the circumstances common\nto all the trials. On the contrary, we recognize in the determining\ncircumstances of their occurrence an extraneous\nelement, an element, that is, extraneous to the idea of the\ngenus and species. Contingency and limitation come in (so\nto speak) together; and both alike disappear when we consider\nthe genus in its entirety, or (which is the same thing)\nin what may be called an ideal and practically impossible\nrealization of all which it potentially contains. If this be\ngranted, it seems to follow that the fundamental principle\nof the Theory of Probabilities may be regarded as included\nin the following statement,--The conception of a genus\nimplies that of numerical relations among the species subordinated\nto it.\" As remarked above, this appears a substantially\nsimilar doctrine to that explained in this chapter,\nbut I do not think that the terms genus and species are by\nany means so well fitted to bring out the conception of a\ntendency or limit as when we speak of a series, and I therefore\nmuch prefer the latter expression.\n\n6. The reader will now have in his mind the conception\nof a series or group of things or events, about the individuals\nof which we know but little, at least in certain respects,\nwhilst we find a continually increasing uniformity as we\ntake larger numbers under our notice. This is definite\nenough to point out tolerably clearly the kind of things\nwith which we have to deal, but it is not sufficiently definite\nfor purposes of accurate thought. We must therefore attempt\na somewhat closer analysis.\n\nThere are certain phrases so commonly adopted as to\nhave become part of the technical vocabulary of the subject,\nsuch as an 'event' and the 'way in which it can\nhappen.' Thus the act of throwing a penny would be called\nan event, and the fact of its giving head or tail would be\ncalled the way in which the event happened. If we were\ndiscussing tables of mortality, the former term would denote\nthe mere fact of death, the latter the age at which\nit occurred, or the way in which it was brought about,\nor whatever else in it might be the particular circumstance\nunder discussion. This phraseology is very convenient, and\nwill often be made use of in this work, but without explanation\nit may lead to confusion. For in many cases the\nway in which the event happens is of such great relative\nimportance, that according as it happens in one way or\nanother the event would have a different name; in other\nwords, it would not in the two cases be nominally the same\nevent. The phrase therefore will have to be considerably\nstretched before it will conveniently cover all the cases to\nwhich we may have to apply it. If for instance we were\ncontemplating a series of human beings, male and female,\nit would sound odd to call their humanity an event, and\ntheir sex the way in which the event happened.\n\nIf we recur however to any of the classes of objects\nalready referred to, we may see our path towards obtaining\na more accurate conception of what we want. It will easily\nbe seen that in every one of them there is a mixture of\nsimilarity and dissimilarity; there is a series of events\nwhich have a certain number of features or attributes in\ncommon,--without this they would not be classed together.\nBut there is also a distinction existing amongst them; a\ncertain number of other attributes are to be found in some\nand are not to be found in others. In other words, the\nindividuals which form the series are compound, each being\nmade up of a collection of things or attributes; some of\nthese things exist in all the members of the series, others\nare found in some only. So far there is nothing peculiar\nto the science of Probability; that in which the distinctive\ncharacteristic consists is this;--that the occasional attributes,\nas distinguished from the permanent, are found on\nan extended examination to tend to exist _in a certain definite\nproportion of the whole number of cases_. We cannot tell in\nany given instance whether they will be found or not, but\nas we go on examining more cases we find a growing uniformity.\nWe find that the proportion of instances in which\nthey are found to instances in which they are wanting, is\ngradually subject to less and less comparative variation, and\napproaches continually towards some apparently fixed value.\n\nThe above is the most comprehensive form of description;\nas a matter of fact the groups will in many cases take a\nfar simpler form; they may appear, e.g. simply as a succession\nof things of the same kind, say human beings, with\nor without an occasional attribute, say that of being left-handed.\nWe are using the word attribute, of course, in its\nwidest sense, intending it to include every distinctive feature\nthat can be observed in a thing, from essential qualities\ndown to the merest accidents of time and place.\n\n7. On examining our series, therefore, we shall find\nthat it may best be conceived, not necessarily as a succession\nof events happening in different ways, but as a succession\nof groups of things. These groups, on being analysed, are\nfound in every case to be resolvable into collections of substances\nand attributes. That which gives its unity to the\nsuccession of groups is the fact of some of these substances or\nattributes being common to the whole succession; that which\ngives their distinction to the groups in the succession is the\nfact of some of them containing only a portion of these substances\nand attributes, the other portion or portions being\noccasionally absent. So understood, our phraseology may\nbe made to embrace every class of things of which Probability\ncan take account.\n\n8. It will be easily seen that the ordinary expression\n(viz. the 'event,' and the 'way in which it happens') may be\nincluded in the above. When the occasional attributes are\nunimportant the permanent ones are sufficient to fix and\nappropriate the name, the presence or absence of the others\nbeing simply denoted by some modification of the name or\nthe addition of some predicate. We may therefore in all such\ncases speak of the collection of attributes as 'the event,'--the\nsame event essentially, that is--only saying that _it_ (so as\nto preserve its nominal identity) happens in different ways\nin the different cases. When the occasional attributes however\nare important, or compose the majority, this way of\nspeaking becomes less appropriate; language is somewhat\nstrained by our implying that two extremely different assemblages\nare in reality the same event, with a difference only\nin its mode of happening. The phrase is however a very\nconvenient one, and with this caution against its being misunderstood,\nit will frequently be made use of here.\n\n9. A series of the above-mentioned kind is, I apprehend,\nthe ultimate basis upon which all the rules of\nProbability must be based. It is essential to a clear comprehension\nof the subject to have carried our analysis up\nto this point, but any attempt at further analysis into the\nintimate nature of the events composing the series, is not\nrequired. It is altogether unnecessary, for instance, to form\nany opinion upon the questions discussed in metaphysics as\nto the independent existence of substances. We have discovered,\non examination, a series composed of groups of\nsubstances and attributes, or of attributes alone. At such\na series we stop, and thence investigate our rules of inference;\ninto what these substances or attributes would themselves\nbe ultimately analysed, if taken in hand by the\npsychologist or metaphysician, it is no business of ours to\nenquire here.\n\n10. The stage then which we have now reached is\nthat of having discovered a quantity of things (they prove\non analysis to be groups of things) which are capable of\nbeing classified together, and are best regarded as constituting\na series. The distinctive peculiarity of this series is\nour finding in it an order, gradually emerging out of disorder,\nand showing in time a marked and unmistakeable uniformity.\n\nThe impression which may possibly be derived from the\ndescription of such a series, and which the reader will probably\nalready entertain if he have studied Probability before,\nis that the gradual evolution of this order is indefinite, and\nits approach therefore to perfection unlimited. And many of\nthe examples commonly selected certainly tend to confirm\nsuch an impression. But in reference to the theory of the\nsubject it is, I am convinced, an error, and one liable to lead\nto much confusion.\n\nThe lines which have been prefixed as a motto to this\nwork, \"So careful of the type she seems, so careless of the\nsingle life,\" are soon after corrected by the assertion that\nthe type itself, if we regard it for a long time, changes,\nand then vanishes and is succeeded by others. So in Probability;\nthat uniformity which is found in the long run,\nand which presents so great a contrast to the individual\ndisorder, though durable is not everlasting. Keep on watching\nit long enough, and it will be found almost invariably to\nfluctuate, and in time may prove as utterly irreducible to\nrule, and therefore as incapable of prediction, as the individual\ncases themselves. The full bearing of this fact upon\nthe theory of the subject, and upon certain common modes\nof calculation connected with it, will appear more fully in\nsome of the following chapters; at present we will confine\nourselves to very briefly establishing and illustrating it.\n\nLet us take, for example, the average duration of life.\nThis, provided our data are sufficiently extensive, is known to\nbe tolerably regular and uniform. This fact has been already\nindicated in the preceding sections, and is a truth indeed\nof which the popular mind has a tolerably clear grasp at the\npresent day. But a very little consideration will show that\nthere may be a superior as well as an inferior limit to\nthe extent within which this uniformity can be observed;\nin other words whilst we may fall into error by taking too\nfew instances we may also fail in our aim, though in a very\ndifferent way and from quite different reasons, by taking too\nmany. At the present time the average duration of life in\nEngland may be, say, forty years; but a century ago it was\ndecidedly less; several centuries ago it was presumably very\nmuch less; whilst if we possessed statistics referring to a still\nearlier population of the country we should probably find that\nthere has been since that time a still more marked improvement.\nWhat may be the future tendency no man can say for\ncertain. It may be, and we hope that it will be the case,\nthat owing to sanitary and other improvements, the duration\nof life will go on increasing steadily; it is at least conceivable,\nthough doubtless incredible, that it should do so without\nlimit. On the other hand, and with much more likelihood,\nthis duration might gradually tend towards some fixed\nlength. Or, again, it is perfectly possible that future generations\nmight prefer a short and a merry life, and therefore\nreduce their average longevity. The duration of life cannot\nbut depend to some extent upon the general tastes, habits\nand employments of the people, that is upon the ideal which\nthey consciously or unconsciously set before them, and he would\nbe a rash man who should undertake to predict what this ideal\nwill be some centuries hence. All that it is here necessary\nhowever to indicate is, that this particular uniformity (as we\nhave hitherto called it, in order to mark its relative character)\nhas varied, and, under the influence of future eddies\nin opinion and practice, may vary still; and this to any\nextent, and with any degree of irregularity. To borrow a\nterm from Astronomy, we find our uniformity subject to what\nmight be called an irregular _secular_ variation.\n\n11. The above is a fair typical instance. If we had\ntaken a less simple feature than the length of life, or one\nless closely connected with what may be called by comparison\nthe great permanent uniformities of nature, we should\nhave found the peculiarity under notice exhibited in a far\nmore striking degree. The deaths from small-pox, for example,\nor the instances of duelling or accusations of witchcraft,\nif examined during a few successive decades, might\nhave shown a very tolerable degree of uniformity. But these\nuniformities have risen possibly from zero; after various and\nvery great fluctuations seem tending towards zero again, at\nleast in this century; and may, for anything we know, undergo\nstill more rapid fluctuations in future. Now these\nexamples must be regarded as being only extreme ones, and\nnot such very extreme ones, of what is the almost universal\nrule in nature. I shall endeavour to show that even the few\napparent exceptions, such as the proportions between male\nand female births, &c., may not be, and probably in reality\nare not, strictly speaking, exceptions. A type, that is, which\nshall be in the fullest sense of the words, persistent and\ninvariable is scarcely to be found in nature. The full import\nof this conclusion will be seen in future chapters. Attention\nis only directed here to the important inference that, although\nstatistics are notoriously of no value unless they are in sufficient\nnumbers, yet it does not follow but that in certain cases\nwe may have too many of them. If they are made too extensive,\nthey may again fall short, at least for any particular\ntime or place, of their greatest attainable accuracy.\n\n12. These natural uniformities then are found at\nlength to be subject to fluctuation. Now contrast with them\nany of the uniformities afforded by games of chance; these\nlatter seem to show no trace of secular fluctuation, however\nlong we may continue our examination of them. Criticisms\nwill be offered, in the course of the following chapters, upon\nsome of the common attempts to prove _\u00e0 priori_ that there\nmust be this fixity in the uniformity in question, but of its\nexistence there can scarcely be much doubt. Pence give\nheads and tails about equally often now, as they did when\nthey were first tossed, and as we believe they will continue\nto do, so long as the present order of things continues. The\nfixity of these uniformities may not be as absolute as is\ncommonly supposed, but no amount of experience which we\nneed take into account is likely in any appreciable degree to\ninterfere with them. Hence the obvious contrast, that,\nwhereas natural uniformities at length fluctuate, those afforded\nby games of chance seem fixed for ever.\n\n13. Here then are series apparently of two different\nkinds. They are alike in their initial irregularity, alike in\ntheir subsequent regularity; it is in what we may term\ntheir ultimate form that they begin to diverge from each\nother. The one tends without any irregular variation\ntowards a fixed numerical proportion in its uniformity; in\nthe other the uniformity is found at last to fluctuate, and to\nfluctuate, it may be, in a manner utterly irreducible to rule.\n\nAs this chapter is intended to be little more than explanatory\nand illustrative of the foundations of the science,\nthe remark may be made here (for which subsequent justification\nwill be offered) that it is in the case of series of the\nformer kind only that we are able to make anything which\ncan be interpreted into strict scientific inferences. We shall\nbe able however in a general way to see the kind and extent\nof error that would be committed if, in any example, we were\nto substitute an imaginary series of the former kind for any\nactual series of the latter kind which experience may present\nto us. The two series are of course to be as alike as possible\nin all respects, except that the variable uniformity has been\nreplaced by a fixed one. The difference then between them\nwould not appear in the initial stage, for in that stage the\ndistinctive characteristics of the series of Probability are not\napparent; all is there irregularity, and it would be as impossible\nto show that they were alike as that they were\ndifferent; we can only say generally that each shows the\nsame kind of irregularity. Nor would it appear in the next\nsubsequent stage, for the real variability of the uniformity\nhas not for some time scope to make itself perceived. It\nwould only be in what we have called the ultimate stage,\nwhen we suppose the series to extend for a very long time,\nthat the difference would begin to make itself felt.[3] The\nproportion of persons, for example, who die each year at the\nage of six months is, when the numbers examined are on a\nsmall scale, utterly irregular; it becomes however regular\nwhen the numbers examined are on a larger scale; but if we\ncontinued our observation for a very great length of time, or\nover a very great extent of country, we should find this\nregularity itself changing in an irregular way. The substitution\njust mentioned is really equivalent to saying, Let\nus assume that the regularity is fixed and permanent. It is\nmaking a hypothesis which may not be altogether consistent\nwith fact, but which is forced upon us for the purpose of\nsecuring precision of statement and definition.\n\n14. The full meaning and bearing of such a substitution\nwill only become apparent in some of the subsequent\nchapters, but it may be pointed out at once that it is in this\nway only that we can with perfect strictness introduce the\nnotion of a 'limit' into our account of the matter, at any\nrate in reference to many of the applications of the subject\nto purely statistical enquiries. We say that a certain proportion\nbegins to prevail among the events in the long run;\nbut then on looking closer at the facts we find that we have\nto express ourselves hypothetically, and to say that if present\ncircumstances remain as they are, the long run will show its\ncharacteristics without disturbance. When, as is often the\ncase, we know nothing accurately of the circumstances by\nwhich the succession of events is brought about, but have\nstrong reasons to suspect that these circumstances are likely\nto undergo some change, there is really nothing else to be\ndone. We can only introduce the conception of a limit, towards\nwhich the numbers are tending, by assuming that\nthese circumstances do not change; in other words, by substituting\na series with a fixed uniformity for the actual one\nwith the varying uniformity.[4]\n\n15. If the reader will study the following example,\none well known to mathematicians under the name of the\nPetersburg[5] problem, he will find that it serves to illustrate\nseveral of the considerations mentioned in this chapter. It\nserves especially to bring out the facts that the series with\nwhich we are concerned must be regarded as indefinitely\nextensive in point of number or duration; and that when so\nregarded certain series, but certain series only (the one in\nquestion being a case in point), take advantage of the indefinite\nrange to keep on producing individuals in it whose\ndeviation from the previous average has no finite limit\nwhatever. When rightly viewed it is a very simple problem,\nbut it has given rise, at one time or another, to a good\ndeal of confusion and perplexity.\n\nThe problem may be stated thus:--a penny is tossed up;\nif it gives head I receive one pound; if heads twice running\ntwo pounds; if heads three times running four pounds, and\nso on; the amount to be received doubling every time that\na fresh head succeeds. That is, I am to go on as long as it\ncontinues to give a succession of heads, to regard this succession\nas a 'turn' or set, and then take another turn, and so\non; and for each such turn I am to receive a payment; the\noccurrence of tail being understood to yield nothing, in fact\nbeing omitted from our consideration. However many times\nhead may be given in succession, the number of pounds I\nmay claim is found by raising two to a power one less\nthan that number of times. Here then is a series formed by\na succession of throws. We will assume,--what many persons\nwill consider to admit of demonstration, and what\ncertainly experience confirms within considerable limits,--that\nthe rarity of these 'runs' of the same face is in direct\nproportion to the amount I receive for them when they do\noccur. In other words, if we regard only the occasions on\nwhich I receive payments, we shall find that every other\ntime I get one pound, once in four times I get two pounds,\nonce in eight times four pounds, and so on without any end.\nThe question is then asked, what ought I to pay for this\nprivilege? At the risk of a slight anticipation of the results\nof a subsequent chapter, we may assume that this is equivalent\nto asking, what amount paid each time would on the\naverage leave me neither winner nor loser? In other words,\nwhat is the average amount I should receive on the above\nterms? Theory pronounces that I ought to give an _infinite_\nsum: that is, no finite sum, however great, would be an\nadequate equivalent. And this is really quite intelligible.\nThere is a series of indefinite length before me, and the\nlonger I continue to work it the richer are my returns, and\nthis without any limit whatever. It is true that the very\nrich hauls are extremely rare, but still they do come, and\nwhen they come they make it up by their greater richness.\nOn every occasion on which people have devoted themselves\nto the pursuit in question, they made acquaintance, of course,\nwith but a limited portion of this series; but the series on\nwhich we base our calculation is unlimited; and the inferences\nusually drawn as to the sum which ought in the long\nrun to be paid for the privilege in question are in perfect\naccordance with this supposition.\n\nThe common form of objection is given in the reply, that\nso far from paying an infinite sum, no sensible man would\ngive anything approaching to \u00a350 for such a chance. Probably\nnot, because no man would see enough of the series to\nmake it worth his while. What most persons form their\npractical opinion upon, is such small portions of the series\nas they have actually seen or can reasonably expect. Now\nin any such portion, say one which embraces 100 turns, the\nlongest succession of heads would not amount on the average\nto more than seven or eight. This is observed, but it is forgotten\nthat the formula which produced these, would, if it\nhad greater scope, keep on producing better and better ones\nwithout any limit. Hence it arises that some persons are\nperplexed, because the conduct they would adopt, in reference\nto the curtailed portion of the series which they are practically\nlikely to meet with, does not find its justification in inferences\nwhich are necessarily based upon the series in the completeness\nof its infinitude.\n\n16. This will be more clearly seen by considering the\nvarious possibilities, and the scope required in order to exhaust\nthem, when we confine ourselves to a _limited_ number of\nthrows. Begin with three. This yields eight equally likely\npossibilities. In four of these cases the thrower starts with\ntail and therefore loses: in two he gains a single point\n(i.e. \u00a31); in one he gains two points, and in one he gains four\npoints. Hence his total gain being eight pounds achieved in\nfour different contingencies, his average gain would be two\npounds.\n\nNow suppose he be allowed to go as far as n throws, so\nthat we have to contemplate 2^{n} possibilities. All of these\nhave to be taken into account if we wish to consider what\nhappens on the average. It will readily be seen that, when\nall the possible cases have been reckoned once, his total gain\nwill be (reckoned in pounds),\n\n2^{n-2} + 2^{n-3}\u00b72 + 2^{n-4}\u00b72^{2} + ... + 2\u00b72^{n-3} + 2^{n-2} + 2^{n-1},\n\nviz.\n\n(n + 1) 2^{n-2}.\n\nThis being spread over 2^{n-1} different occasions of gain his\naverage gain will be 1/2 (n + 1).\n\nNow when we are referring to averages it must be remembered\nthat the minimum number of different occurrences\nnecessary in order to justify the average is that which enables\neach of them to present itself once. A man proposes to stop\nshort at a succession of ten heads. Well and good. We tell\nhim that his average gain will be \u00a35. 10_s_. 0_d_.: but we also\nimpress upon him that in order to justify this statement he\nmust commence to toss at least 1024 times, for in no less\nnumber can all the contingencies of gain and loss be exhibited\nand balanced. If he proposes to reach an average gain of \u00a320,\nhe will require to be prepared to go up to 39 throws,\nTo _justify_ this payment he must commence to throw 2^{39} times,\ni.e. about a million million times. Not before he has\naccomplished this will he be in a position to prove to any\nsceptic that this is the true average value of a 'turn' extending\nto 39 successive tosses.\n\nOf course if he elects to toss to all eternity we must\nadopt the line of explanation which alone is possible where\nquestions of infinity in respect of number and magnitude are\ninvolved. We cannot tell him to pay down 'an infinite sum,'\nfor this has no strict meaning. But we tell him that, however\nmuch he may consent to pay each time runs of heads occur,\nhe will attain at last a stage in which he will have won\nback his total payments by his total receipts. However\nlarge n may be, if he perseveres in trying 2^{n} times he _may_\nhave a true average receipt of 1/2 (n + 1) pounds, and if he\ncontinues long enough onwards he _will_ have it.\n\nThe problem will recur for consideration in a future\nchapter.\n\n\n1. The following statistics will give a fair idea of the wide range of\n  experience over which such regularity is found to exist: \"As\n  illustrations of equal amounts of fluctuation from totally\n  dissimilar causes, take the deaths in the West district of London in\n  seven years (fluctuation 13.66), and offences against the person\n  (fluctuation 13.61); or deaths from apoplexy (fluctuation 5.54), and\n  offences against property, without violence (fluctuation 5.48); or\n  students registered at the College of Surgeons (fluctuation 1.85),\n  and the number of pounds of manufactured tobacco taken for home\n  consumption (fluctuation 1.89); or out-door paupers (fluctuation\n  3.45) and tonnage of British vessels entered in ballast (fluctuation\n  3.43), &c.\"  [Extracted from a paper in the Journal of the\n  Statistical Society, by Mr Guy, March, 1858; the 'fluctuation' here\n  given is a measure of the amount of irregularity, that is of\n  departure from the average, estimated in a way which will be\n  described hereafter.]\n\n2. Transactions of the Cambridge Philosophical Society, Vol. IX. p. 605.\n  Reprinted in the collected edition of his writings, p. 50.\n\n3. We might express it thus:--a few instances are not sufficient to\n  display a law at all; a considerable number will suffice to display\n  it; but it takes a very great number to establish that a _change_ is\n  taking place in the law.\n\n4. The mathematician may illustrate the nature of this substitution by\n  the analogies of the 'circle of curvature' in geometry, and the\n  'instantaneous ellipse' in astronomy. In the cases in which these\n  conceptions are made use of we have a phenomenon which is\n  continuously varying and also changing its rate of variation. We\n  take it at some given moment, suppose its rate at that moment to be\n  fixed, and then complete its career on that supposition.\n\n5. So called from its first mathematical treatment appearing in the\n  _Commentarii_ of the Petersburg Academy; a variety of notices upon\n  it will be found in Mr Todhunter's History of the Theory of\n  Probability.\n\n\n\n\nCHAPTER II.\n\n\n_FURTHER DISCUSSION UPON THE NATURE OF THE SERIES MENTIONED IN THE LAST\nCHAPTER._\n\n1. In the course of the last chapter the nature of a particular\nkind of series, that namely, which must be considered\nto constitute the basis of the science of Probability, has received\na sufficiently general explanation for the preliminary\npurpose of introduction. One might indeed say more than\nthis; for the characteristics which were there pointed out are\nreally sufficient in themselves to give a fair general idea of\nthe nature of Probability, and of the sort of problems with\nwhich it deals. But in the concluding paragraphs an indication\nwas given that the series of this kind, as they actually\noccur in nature or as the results of more or less artificial\nproduction, are seldom or never found to occur in such a\nsimple form as might possibly be expected from what had\npreviously been said; but that they are almost always seen\nto be associated together in groups after a somewhat complicated\nfashion. A fuller discussion of this topic must now\nbe undertaken.\n\nWe will take for examination an instance of a kind with\nwhich the investigations of Quetelet will have served to\nfamiliarize some readers. Suppose that we measure the\nheights of a great many adult men in any town or country.\nThese heights will of course lie between certain extremes in\neach direction, and if we continue to accumulate our measures\nit will be found that they tend to lie continuously\nbetween these extremes; that is to say, that under those\ncircumstances no intermediate height will be found to be\npermanently unrepresented in such a collection of measurements.\nNow suppose these heights to be marshalled in the\norder of their magnitude. What we always find is something\nof the following kind;--about the middle point between\nthe extremes, a large number of the results will be\nfound crowded together: a little on each side of this point\nthere will still be an excess, but not to so great an extent;\nand so on, in some diminishing scale of proportion, until as\nwe get towards the extreme results the numbers thin off and\nbecome relatively exceedingly small.\n\nThe point to which attention is here directed is not the\nmere fact that the numbers thus tend to diminish from the\nmiddle in each direction, but, as will be more fully explained\ndirectly, the _law_ according to which this progressive diminution\ntakes place. The word 'law' is here used in its mathematical\nsense, to express the formula connecting together the\ntwo elements in question, namely, the height itself, and the\nrelative number that are found of that height. We shall\nhave to enquire whether one of these elements is a function\nof the other, and, if so, what function.\n\n2. After what was said in the last chapter, it need\nhardly be insisted upon that the interest and significance of\nsuch investigations as these are almost entirely dependent\nupon the statistics being very extensive. In one or other of\nQuetelet's works on Social Physics[1] will be found a selection\nof measurements of almost every element which the physical\nframe of man can furnish:--his height, his weight, the muscular\npower of various limbs, the dimensions of almost every\npart and organ, and so on. Some of the most extensive of\nthese express the heights of 25,000 Federal soldiers from the\nArmy of the Potomac, and the circumferences of the chests\nof 5738 Scotch militia men taken many years ago. Those\nwho wish to consult a large repertory of such statistics cannot\nbe referred to any better sources than to these and other\nworks by the same author.[2]\n\nInteresting and valuable, however, as are Quetelet's statistical\ninvestigations (and much of the importance now\ndeservedly attached to such enquiries is, perhaps, owing\nmore to his efforts than to those of any other person), I cannot\nbut feel convinced that there is much in what he has\nwritten upon the subject which is erroneous and confusing as\nregards the foundations of the science of Probability, and the\nphilosophical questions which it involves. These errors are\nnot by any means confined to him, but for various reasons\nthey will be better discussed in the form of a criticism of his\nexplicit or implicit expression of them, than in any more independent\nway.\n\n3. In the first place then, he always, or almost always,\nassumes that there can be but one and the same law of arrangement\nfor the results of our observations, measurements,\nand so on, in these statistical enquiries. That is, he assumes\nthat whenever we get a group of such magnitudes\nclustering about a mean, and growing less frequent as\nthey depart from that mean, we shall find that this diminution\nof frequency takes place according to one invariable\nlaw, whatever may be the nature of these magnitudes,\nand whatever the process by which they may have\nbeen obtained.\n\nThat such a uniformity as this should prevail amongst\nmany and various classes of phenomena would probably seem\nsurprising in any case. But the full significance of such a\nfact as this (if indeed it were a fact) only becomes apparent\nwhen attention is directed to the profound distinctions in the\nnature and origin of the phenomena which are thus supposed\nto be harmonized by being brought under one comprehensive\nprinciple. This will be better appreciated if we take a brief\nglance at some of the principal classes into which the things\nwith which Probability is chiefly concerned may be divided.\nThese are of a three-fold kind.\n\n4. In the first place there are the various combinations,\nand runs of luck, afforded by games of chance. Suppose\na handful, consisting of ten coins, were tossed up a\ngreat many times in succession, and the results were tabulated.\nWhat we should obtain would be something of the\nfollowing kind. In a certain proportion of cases, and these\nthe most numerous of all, we should find that we got five\nheads and five tails; in a somewhat less proportion of cases\nwe should have, as equally frequent results, four heads six\ntails, and four tails six heads; and so on in a continually\ndiminishing proportion until at length we came down, in a\nvery small relative number of cases, to nine heads one tail,\nand nine tails one head; whilst the least frequent results\npossible would be those which gave all heads or all tails.[3]\nHere the statistical elements under consideration are, as\nregards their origin at any rate, optional or brought about\nby human choice. They would, therefore, be commonly\ndescribed as being mainly artificial, but their results ultimately\naltogether a matter of chance.\n\nAgain, in the second place, we might take the accurate\nmeasurements--i.e. the actual magnitudes themselves,--of\na great many natural objects, belonging to the same genus\nor class; such as the cases, already referred to, of the heights,\nor other characteristics of the inhabitants of any district.\nHere human volition or intervention of any kind seem to\nhave little or nothing to do with the matter. It is optional\nwith us to _collect_ the measures, but the things measured are\nquite outside our control. They would therefore be commonly\ndescribed as being altogether the production of nature,\nand it would not be supposed that in strictness chance had\nanything whatever to do with the matter.\n\nIn the third place, the result at which we are aiming\nmay be some fixed magnitude, one and the same in each\nof our successive attempts, so that if our measurements\nwere rigidly accurate we should merely obtain the same\nresult repeated over and over again. But since all our\nmethods of attaining our aims are practically subject to\ninnumerable imperfections, the results actually obtained\nwill depart more or less, in almost every case, from the\nreal and fixed value which we are trying to secure. They\nwill be sometimes more wide of the mark, sometimes less\nso, the worse attempts being of course the less frequent.\nIf a man aims at a target he will seldom or never hit it\nprecisely in the centre, but his good shots will be more[4]\nnumerous than his bad ones. Here again, then, we have\na series of magnitudes (i.e. the deflections of the shots from\nthe point aimed at) clustering about a mean, but produced\nin a very different way from those of the last two cases.\nIn this instance the elements would be commonly regarded\nas only partially the results of human volition, and chance\ntherefore as being only a co-agent in the effects produced.\nWith these must be classed what may be called _estimates_,\nas distinguished from measurements. By the latter are\ngenerally understood the results of a certain amount of\nmechanism or manipulation; by the former we may understand\nthose cases in which the magnitude in question is\ndetermined by direct observation or introspection. The\ninterest and importance of this class, so far as scientific\nprinciples are concerned, dates mainly from the investigations\nof Fechner. Its chief field is naturally to be found amongst\npsychological data.\n\nOther classes of things, besides those alluded to above,\nmight readily be given. These however are the classes about\nwhich the most extensive statistics are obtainable, or to\nwhich the most practical importance and interest are attached.\nThe profound distinctions which separate their\norigin and character are obvious. If they all really did\ndisplay precisely the same law of variation it would be a\nmost remarkable fact, pointing doubtless to some deep-seated\nidentity underlying the various ways, apparently\nso widely distinct, in which they had been brought about.\nThe questions now to be discussed are: Is it the case,\nwith any considerable degree of rigour, that only one law\nof distribution does really prevail? and, in so far as this\nis so, how does it come to pass?\n\n5. In support of an affirmative answer to the former\nof these two questions, several different kinds of proof are,\nor might be, offered.\n\n(I.) For one plan we may make a direct appeal to\nexperience, by collecting sets of statistics and observing\nwhat is their law of distribution. As remarked above, this\nhas been done in a great variety of cases, and in some\ninstances to a very considerable extent, by Quetelet and\nothers. His researches have made it abundantly convincing\nthat many classes of things and processes, differing widely\nin their nature and origin, do nevertheless appear to conform\nwith a considerable degree of accuracy to one and the\nsame[5] law. At least this is made plain for the more\ncentral values, for those that is which are situated most\nnearly about the mean. With regard to the extreme values\nthere is, on the other hand, some difficulty. For instance\nin the arrangements of the heights of a number of men,\nthese extremes are rather a stumbling-block; indeed it has\nbeen proposed to reject them from both ends of the scale\non the plea that they are monstrosities, the fact being that\ntheir relative numbers do not seem to be by any means\nthose which theory would assign.[6] Such a plan of rejection\nis however quite unauthorized, for these dwarfs and giants\nare born into the world like their more normally sized\nbrethren, and have precisely as much right as any others\nto be included in the formul\u00e6 we draw up.\n\nBesides the instance of the heights of men, other classes\nof observations of a somewhat similar character have been\nalready referred to as collected and arranged by Quetelet.\nFrom the nature of the case, however, there are not many\nappropriate ones at hand; for when our object is, not to\nillustrate a law which can be otherwise proved, but to\nobtain actual direct proof of it, the collection of observations\nand measurements ought to be made upon such a large\nscale as to deter any but the most persevering computers\nfrom undergoing the requisite labour. Some of the remarks\nmade in the course of the note on the opposite page will\nserve to illustrate the difficulties which would lie in the way\nof such a mode of proof.\n\nWe are speaking here, it must be understood, only of\n_symmetrical_ curves: if there is asymmetry, i.e. if the Law of\nError is different on different sides of the mean,--a comparatively\nvery small number of observations would suffice\nto detect the fact. But, granted symmetry and rapid\ndecrease of frequency on each side of the mean, we could\ngenerally select some one species of the exponential curve\nwhich should pretty closely represent our statistics in the\nneighbourhood of the mean. That is, where the statistics are\nnumerous we could secure agreement; and where we could\nnot secure agreement the statistics would be comparatively\nso scarce that we should have to continue the observations\nfor a very long time in order to prove the disagreement.\n\n6. Allowing the various statistics such credit as they\ndeserve, for their extent, appropriateness, accuracy and so\non, the general conclusion which will on the whole be drawn\nby almost every one who takes the trouble to consult them,\nis that they do, in large part, conform approximately to one\ntype or law, at any rate for all except the extreme values.\nSo much as this must be fully admitted. But that they do\nnot, indeed we may say that they cannot, always do so in\nthe case of the extreme values, will become obvious on\na little consideration. In some of the classes of things to\nwhich the law is supposed to apply, for example, the successions\nof heads and tails in the throws of a penny, there is\nno limit to the magnitude of the fluctuations which may and\nwill occur. Postulate as long a succession of heads or of tails\nas we please, and if we could only live and toss long enough\nfor it we should succeed in getting it at length. In other\ncases, including many of the applications of Probability\nto natural phenomena, there can hardly fail to be such\nlimits. Deviations exceeding a certain range may not be\nmerely improbable, that is of very rare occurrence, but they\nmay often from the nature of the case be actually impossible.\nAnd even when they are not actually impossible it\nmay frequently appear on examination that they are only\nrendered possible by the occasional introduction of agencies\nwhich are not supposed to be available in the production\nof the more ordinary or intermediate values. When, for\ninstance, we are making observations with any kind of\ninstrument, the nature of its construction may put an\nabsolute limit upon the possible amount of error. And even\nif there be not an absolute limit under all kinds of usage\nit may nevertheless be the case that there is one under\nfair and proper usage; it being the case that only when\nthe instrument is designedly or carelessly tampered with will\nany new causes of divergence be introduced which were not\nconfined within the old limits.\n\nSuppose, for instance, that a man is firing at a mark.\nHis worst shots must be supposed to be brought about by\na combination of such causes as were acting, or prepared\nto act, in every other case; the extreme instance of what\nwe may thus term 'fair usage' being when a number of\ndistinct causes have happened to conspire together so as\nto tend in the same direction, instead of, as in the other\ncases, more or less neutralizing one another's work. But\nthe aggregate effect of such causes may well be supposed\nto be limited. The man will not discharge his shot nearly\nat right angles to the true line of fire unless some entirely\nnew cause comes in, as by some unusual circumstance\nhaving distracted his attention, or by his having had some\nspasmodic seizure. But influences of this kind were not\nsupposed to have been available before; and even if they\nwere we are taking a bold step in assuming that these\noccasional great disturbances are subject to the same kind\nof laws as are the aggregates of innumerable little ones.\n\nWe cannot indeed lay much stress upon an example\nof this last kind, as compared with those in which we\ncan see for certain that there is a fixed limit to the range\nof error. It is therefore offered rather for illustration than\nfor proof. The enormous, in fact inconceivable magnitude\nof the numbers expressive of the chance of very rare combinations,\nsuch as those in question, has such a bewildering\neffect upon the mind that one may be sometimes apt to confound\nthe impossible with the higher degrees of the merely\nmathematically improbable.\n\n7. At the time the first edition of this essay was composed\nwriters on Statistics were, I think, still for the most\npart under the influence of Quetelet, and inclined to overvalue\nhis authority on this particular subject: of late however\nattention has been repeatedly drawn to the necessity of\ntaking account of other laws of arrangement than the binomial\nor exponential.\n\nMr Galton, for instance,--to whom every branch of the\ntheory of statistics owes so much,--has insisted[7] that the\n\"assumption which lies at the basis of the well-known law of\n'Frequency of Error'... is incorrect in many groups of vital\nand social phenomena.... For example, suppose we endeavour\nto match a tint; Fechner's law, in its approximative and\nsimplest form of sensation = log stimulus, tells us that a\nseries of tints, in which the quantities of white scattered on a\nblack ground are as 1, 2, 4, 8, 16, 32, &c., will appear to the\neye to be separated by equal intervals of tint. Therefore, in\nmatching a grey that contains 8 portions of white, we are\njust as likely to err by selecting one that has 16 portions as\none that has 4 portions. In the first case there would be an\nerror in excess, of 8; in the second there would be an error,\nin deficiency, of 4. Therefore, an error of the same magnitude\nin excess or in deficiency is not equally probable.\" The consequences\nof this assumption are worked out in a remarkable\npaper by Dr D. McAlister, to which allusion will have to be\nmade again hereafter. All that concerns us here to point out\nis that when the results of statistics of this character are\narranged graphically we do _not_ get a curve which is symmetrical\non both sides of a central axis.\n\n8. More recently, Mr F. Y. Edgeworth (in a report of\na Committee of the British Association appointed to enquire\ninto the variation of the monetary standard) has urged the\nsame considerations in respect of prices of commodities. He\ngives a number of statistics \"drawn from the prices of twelve\ncommodities during the two periods 1782-1820, 1820-1865.\nThe maximum and minimum entry for each series having\nbeen noted, it is found that the number of entries above the\n'middle point,' half-way between the maximum and minimum,[8]\nis in every instance less than half the total number of entries\nin the series. In the twenty-four trials there is not a single\nexception to the rule, and in very few cases even an approach\nto an exception. We may presume then that the curves are\nof the lop-sided character indicated by the accompanying\ndiagram.\" The same facts are also ascertained in respect to\n_place_ variations as distinguished from time variations. To\nthese may be added some statistics of my own, referring to\nthe heights of the barometer taken at the same hour on more\nthan 4000 successive days (v. _Nature_, Sept. 2, 1887). So far\nas these go they show a marked asymmetry of arrangement.\n\nIn fact it appears to me that this want of symmetry\nought to be looked for in all cases in which the phenomena\nunder measurement are of a 'one-sided' character; in the\nsense that they are measured on one side only of a certain\nfixed point from which their possibility is supposed to start.\nFor not only is it impossible for them to fall below this point:\nlong before they reach it the influence of its proximity is felt\nin enhancing the difficulty and importance of the same\namount of absolute difference.\n\nLook at a table of statures, for instance, with a mean\nvalue of 69 inches. A diminution of three feet (were this\npossible) is much more influential,--counts for much more,\nin every sense of the term,--than an addition of the same\namount; for the former does not double the mean, while the\nlatter more than halves it. Revert to an illustration. If\na vast number of petty influencing circumstances of the kind\nalready described were to act upon a swinging _pendulum_ we\nshould expect the deflections in each direction to display\nsymmetry; but if they were to act upon a _spring_ we should\nnot expect such a result. Any phenomena of which the\nlatter is the more appropriate illustration can hardly be\nexpected to range themselves with symmetry about a mean.[9]\n\n9. (II.) The last remarks will suggest another kind of\nproof which might be offered to establish the invariable nature\nof the law of error. It is of a direct deductive kind, not\nappealing immediately to statistics, but involving an enquiry\ninto the actual or assumed nature of the causes by which the\nevents are brought about. Imagine that the event under\nconsideration is brought to pass, in the first place, by some\nfixed cause, or group of fixed causes. If this comprised all\nthe influencing circumstances the event would invariably\nhappen in precisely the same way: there would be no errors\nor deflections whatever to be taken account of. But now\nsuppose that there were also an enormous number of very\nsmall causes which tended to produce deflections; that these\ncauses acted in entire independence of one another; and that\neach of the lot told as often, in the long run, in one direction\nas in the opposite. It is easy[10] to see, in a general way, what\nwould follow from these assumptions. In a very few cases\nnearly all the causes would tell in the same direction; in\nother words, in a very few cases the deflection would be\nextreme. In a greater number of cases, however, it would\nonly be the most part of them that would tell in one direction,\nwhilst a few did what they could to counteract the rest;\nthe result being a comparatively larger number of somewhat\nsmaller deflections. So on, in increasing numbers, till we\napproach the middle point. Here we shall have a very large\nnumber of very small deflections: the cases in which the\nopposed influences just succeed in balancing one another,\nso that no error whatever is produced, being, though actually\ninfrequent, relatively the most frequent of all.\n\nNow if all deflections from a mean were brought about in\nthe way just indicated (an indication which must suffice for\nthe present) we should always have one and the same law of\narrangement of frequency for these deflections or errors, viz.\nthe exponential[11] law mentioned in \u00a75.\n\n10. It may be readily admitted from what we know\nabout the production of events that something resembling\nthese assumptions, and therefore something resembling the\nconsequences which follow from them, is really secured in a\nvery great number of cases. But although this may prevail\napproximately, it is in the highest degree improbable that it\ncould ever be secured, even artificially, with anything approaching\nto rigid accuracy. For one thing, the causes of\ndeflection will seldom or never be really independent of one\nanother. Some of them will generally be of a kind such that\nthe supposition that several are swaying in one direction,\nmay affect the capacity of each to produce that full effect\nwhich it would have been capable of if it had been left to do\nits work alone. In the common example, for instance, of\nfiring at a mark, so long as we consider the case of the tolerably\ngood shots the effect of the wind (one of the causes of\nerror) will be approximately the same whatever may be the\nprecise direction of the bullet. But when a shot is considerably\nwide of the mark the wind can no longer be regarded as\nacting at right angles to the line of flight, and its effect in\nconsequence will not be precisely the same as before. In\nother words, the causes here are not strictly independent, as\nthey were assumed to be; and consequently the results to be\nattributed to each are not absolutely uninfluenced by those\nof the others. Doubtless the effect is trifling here, but I\napprehend that if we were carefully to scrutinize the modes\nin which the several elements of the total cause conspire\ntogether, we should find that the assumption of absolute\nindependence was hazardous, not to say unwarrantable, in a\nvery great number of cases. These brief remarks upon the\nprocess by which the deflections are brought about must\nsuffice for the present purpose, as the subject will receive a\nfuller investigation in the course of the next chapter.\n\nAccording, therefore, to the best consideration which\ncan at the present stage be afforded to this subject, we may\ndraw a similar conclusion from this deductive line of argument\nas from the direct appeal to statistics. The same\ngeneral result seems to be established; namely, that approximately,\nwith sufficient accuracy for all practical purposes, we\nmay say that an examination of the causes by which the\ndeflections are generally brought about shows that they are\nmostly of such a character as would result in giving us the\ncommonly accepted 'Law of Error,' as it is termed.[12] The\ntwo lines of enquiry, therefore, within the limits assigned,\nafford each other a decided mutual confirmation.\n\n11. (III.) There still remains a third, indirect and\nmathematical line of proof, which might be offered to establish\nthe conclusion that the Law of Error is always one and\nthe same. It may be maintained that the recognized and\nuniversal employment of one and the same method, that\nknown to mathematicians and astronomers as the Method of\nLeast Squares, in all manner of different cases with very\nsatisfactory results, is compatible only with the supposition\nthat the errors to which that method is applied must be\ngrouped according to one invariable law. If all 'laws of\nerror' were not of one and the same type, that is, if the\nrelative frequency of large and small divergences (such as we\nhave been speaking of) were not arranged according to one\npattern, how could one method or rule equally suit them all?\n\nIn order to preserve a continuity of treatment, some\nnotice must be taken of this enquiry here, though, as in the\ncase of the last argument, any thorough discussion of the\nsubject is impossible at the present stage. For one thing, it\nwould involve too much employment of mathematics, or at\nany rate of mathematical conceptions, to be suitable for the\ngeneral plan of this treatise: I have accordingly devoted a\nspecial chapter to the consideration of it.\n\nThe main reason, however, against discussing this argument\nhere, is, that to do so would involve the anticipation of\na totally different side of the science of Probability from that\nhitherto treated of. This must be especially insisted upon, as\nthe neglect of it involves much confusion and some error.\nDuring these earlier chapters we have been entirely occupied\nwith laying what may be called the physical foundations of\nProbability. We have done nothing else than establish, in one\nway or another, the existence of certain groups or arrangements\nof things which are found to present themselves in\nnature; we have endeavoured to explain how they come to\npass, and we have illustrated their principal characteristics.\nBut these are merely the foundations of Inference, we have\nnot yet said a word upon the logical processes which are to\nbe erected upon these foundations. We have not therefore\nentered yet upon the _logic_ of chance.\n\n12. Now the way in which the Method of Least Squares\nis sometimes spoken of tends to conceal the magnitude of\nthis distinction. Writers have regarded it as synonymous\nwith the Law of Error, whereas the fact is that the two are\nnot only totally distinct things but that they have scarcely\neven any necessary connection with each other. The Law of\nError is the statement of a physical fact; it simply assigns,\nwith more or less of accuracy, the relative frequency with\nwhich errors or deviations of any kind are found in practice\nto present themselves. It belongs therefore to what may be\ntermed the physical foundations of the science. The Method\nof Least Squares, on the other hand, is not a law at all in the\nscientific sense of the term. It is simply a rule or direction\ninforming us how we may best proceed to treat any group of\nthese errors which may be set before us, so as to extract the\ntrue result at which they have been aiming. Clearly therefore\nit belongs to the inferential or logical part of the subject.\n\nIt cannot indeed be denied that the methods we employ\nmust have some connection with the arrangement of the facts\nto which they are applied; but the two things are none the\nless distinct in their nature, and in this case the connection\ndoes not seem at all a necessary one, but at most one of propriety\nand convenience. The Method of Least Squares is\nusually applied, no doubt, to the most familiar and common\nform of the Law of Error, namely the exponential form with\nwhich we have been recently occupied. But other forms of\nlaws of error may exist, and, if they did, the method in\nquestion might equally well be applied to them. I am not\nasserting that it would necessarily be the best method in\nevery case, but it would be a possible one; indeed we may\ngo further and say, as will be shown in a future chapter,\nthat it would be a good method in almost every case. But\nits particular merits or demerits do not interfere with its\npossible employment in every case in which we may choose\nto resort to it. It will be seen therefore, even from the few\nremarks that can be made upon the subject here, that the\nfact that one and the same method is very commonly employed\nwith satisfactory results affords little or no proof that\nthe errors to which it is applied must be arranged according\nto one fixed law.\n\n13. So much then for the attempt to prove the prevalence,\nin all cases, of this particular law of divergence. The\nnext point in Quetelet's treatment of the subject which deserves\nattention as erroneous or confusing, is the doctrine maintained\nby him and others as to the existence of what he terms a _type_\nin the groups of things in question. This is a not unnatural\nconsequence from some of the data and conclusions of the\nlast few paragraphs. Refer back to two of the three classes\nof things already mentioned in \u00a74. If it really were the case\nthat in arranging in order a series of incorrect observations\nor attempts of our own, and a collection of natural objects\nbelonging to some one and the same species or class, we found\nthat the law of their divergence was in each case identical in\nthe long run, we should be naturally disposed to apply the\nsame expression 'Law of Error' to both instances alike,\nthough in strictness it could only be appropriate to the\nformer. When we perform an operation ourselves with a\nclear consciousness of what we are aiming at, we may quite\ncorrectly speak of every deviation from this as being an\nerror; but when Nature presents us with a group of objects\nof any kind, it is using a rather bold metaphor to speak in\nthis case also of a law of error, as if she had been aiming at\nsomething all the time, and had like the rest of us missed\nher mark more or less in almost every instance.[13]\n\nSuppose we make a long succession of attempts to measure\naccurately the precise height of a man, we should from one\ncause or another seldom or never succeed in doing so with\nabsolute accuracy. But we have no right to assume that these\nimperfect measurements of ours would be found so to deviate\naccording to one particular law of error as to present the\nprecise counterpart of a series of actual heights of _different_\nmen, supposing that these latter were assigned with absolute\nprecision. What might be the actual law of error in a series\nof direct measurements of any given magnitude could hardly\nbe asserted beforehand, and probably the attempt to determine\nit by experience has not been made sufficiently often to\nenable us to ascertain it; but upon general grounds it seems\nby no means certain that it would follow the so-called exponential\nlaw. Be this however as it may, it is rather a\nlicence of language to talk as if nature had been at work in\nthe same way as one of us; aiming (ineffectually for the most\npart) at a given result, that is at producing a man endowed\nwith a certain stature, proportions, and so on, who might\ntherefore be regarded as the typical man.\n\n14. Stated as above, namely, that there is a fixed\ninvariable human type to which all individual specimens of\nhumanity may be regarded as having been meant to attain,\nbut from which they have deviated in one direction or\nanother; according to a law of deviation capable of _\u00e0 priori_\ndetermination, the doctrine is little else than absurd. But\nif we look somewhat closer at the facts of the case, and the\nprobable explanation of these facts, we may see our way to\nan important truth. The facts, on the authority of Quetelet's\nstatistics (the great interest and value of which must be\nfrankly admitted), are very briefly as follows: if we take any\nelement of our physical frame which admits of accurate\nmeasurement, say the height, and determine this measure in\na great number of different individuals belonging to any\ntolerably homogeneous class of people, we shall find that\nthese heights do admit of an orderly arrangement about a\nmean, after the fashion which has been already repeatedly\nmentioned. What is meant by a homogeneous class? is a\npertinent and significant enquiry, but applying this condition\nto any simple cases its meaning is readily stated. It implies\nthat the mean in question will be different according to the\nnationality of the persons under measurement. According to\nQuetelet,[14] in the case of Englishmen the mean is about\n5 ft. 9 in.; for Belgians about 5 ft. 7 in.; for the French about\n5 ft. 4 in. It need hardly be added that these measures are\nthose of adult males.\n\n15. It may fairly be asked here what would have\nbeen the consequence, had we, instead of keeping the English\nand the French apart, mixed the results of our measurements\nof them all together? The question is an important one, as it\nwill oblige us to understand more clearly what we mean by\nhomogeneous classes. The answer that would usually be\ngiven to it, though substantially correct, is somewhat too decisive\nand summary. It would be said that we are here\nmixing distinctly heterogeneous elements, and that in consequence\nthe resultant law of error will be by no means of\nthe simple character previously exhibited. So far as such an\nanswer is to be admitted its grounds are easy to appreciate.\nIn accordance with the usual law of error the divergences\nfrom the mean grow continuously less numerous as they\nincrease in amount. Now, if we mix up the French and\nEnglish heights, what will follow? Beginning from the\nEnglish mean of 5 feet 9 inches, the heights will at first follow\nalmost entirely the law determined by these English\nconditions, for at this point the English data are very numerous,\nand the French by comparison very few. But, as we\nbegin to approach the French mean, the numbers will cease\nto show that continual diminution which they should show,\naccording to the English scale of arrangement, for here the\nFrench data are in turn very numerous, and the English by\ncomparison few. The result of such a combination of heterogeneous\nelements is illustrated by the figure annexed, of\ncourse in a very exaggerated form.\n\n[Figure: Superposition of two Gaussians.]\n\n16. In the above case the nature of the heterogeneity,\nand the reasons why the statistics should be so collected and\narranged as to avoid it, seemed tolerably obvious. It will be\nseen still more plainly if we take a parallel case drawn from\nartificial proceedings. Suppose that after a man had fired a\nfew thousand shots at a certain spot, say a wafer fixed somewhere\non a wall, the position of the spot at which he aims\nwere shifted, and he fired a few thousand more shots at the\nwafer in its new position. Now let us collect and arrange all\nthe shots of both series in the order of their departure from\neither of the centres, say the new one. Here we should\nreally be mingling together two discordant sets of elements,\neither of which, if kept apart from the other, would have\nbeen of a simple and homogeneous character. We should\nfind, in consequence, that the resultant law of error betrayed\nits composite or heterogeneous origin by a glaring departure\nfrom the customary form, somewhat after the fashion indicated\nin the above diagram.\n\nThe instance of the English and French heights resembles\nthe one just given, but falls far short of it in the stringency\nwith which the requisite conditions are secured. The\nfact is we have not here got the most suitable requirements,\nviz. a group consisting of a few fixed causes supplemented by\ninnumerable little disturbing influences. What we call a\nnation is really a highly artificial body, the members of\nwhich are subject to a considerable number of local or occasional\ndisturbing causes. Amongst Frenchmen were included,\npresumably, Bretons, Proven\u00e7als, Alsatians, and so on,\nthus commingling distinctions which, though less than those\nbetween French and English, regarded as wholes, are very\nfar from being insignificant. And to these differences of\nrace must be added other disturbances, also highly important,\ndependent upon varying climate, food and occupation.\nIt is plain, therefore, that whatever objections exist against\nconfusing together French and English statistics, exist also,\nthough of course in a less degree, against confusing together\nthose of the various provincial and other components which\nmake up the French people.\n\n17. Out of the great variety of important causes\nwhich influence the height of men, it is probable that those\nwhich most nearly fulfil the main conditions required by the\n'Law of Error' are those about which we know the least.\nUpon the effects of food and employment, observation has\nsomething to say, but upon the purely physiological causes\nby which the height of the parents influences the height of\nthe offspring, we have probably nothing which deserves to\nbe called knowledge. Perhaps the best supposition we can\nmake is one which, in accordance with the saying that 'like\nbreeds like', would assume that the purely physiological\ncauses represent the constant element; that is, given a homogeneous\nrace of people to begin with, who freely intermarry,\nand are subject to like circumstances of climate, food,\nand occupation, the standard would remain on the whole\nconstant.[15]\n\nIn such a case the man who possessed the mean height,\nmean weight, mean strength, and so on, might then be\ncalled, in a sort of way, a 'type'. The deviations from this\ntype would then be produced by innumerable small influences,\npartly physiological, partly physical and social, acting\nfor the most part independently of one another, and resulting\nin a Law of Error of the usual description. Under such\nrestrictions and explanations as these, there seems to be no\nreasonable objection to speaking of a French or English type\nor mean. But it must always be remembered that under\nthe present circumstances of every political nation, these\nsomewhat heterogeneous bodies might be subdivided into\nvarious smaller groups, each of which would frequently exhibit\nthe characteristics of such a type in an even more\nmarked degree.\n\n18. On this point the reports of the Anthropometrical\nCommittee, already referred to, are most instructive. They\nillustrate the extent to which this subdivision could be\ncarried out, and prove,--if any proof were necessary,--that\nthe discovery of Quetelet's _homme moyen_ would lead us a\nlong chase. So far as their results go the mean 'English'\nstature (in inches) is 67.66. But this is composed of Scotch,\nIrish, English and Welsh constituents, the separate means of\nthese being, respectively; 68.71, 67.90, 67.36, and 66.66.\nBut these again may be subdivided; for careful observation\nshows that the mean English stature is distinctly greater in\ncertain districts (e.g. the North-Eastern counties) than in\nothers. Then again the mean of the professional classes is\nconsiderably greater than that of the labourers; and that of\nthe honest and intelligent is very much greater than that of\nthe criminal and lunatic constituents of the population.\nAnd, so far as the observations are extensive enough for the\npurpose, it appears that every characteristic in respect of the\ngrouping about a mean which can be detected in the more\nextensive of these classes can be detected also in the narrower.\nNor is there any reason to suppose that the same\nprocess of subdivision could not be carried out as much\nfarther as we chose to prolong it.\n\n19. It need hardly be added to the above remarks\nthat no one who gives the slightest adhesion to the Doctrine\nof Evolution could regard the type, in the above qualified\nsense of the term, as possessing any real permanence and\nfixity. If the constant causes, whatever they may be, remain\nunchanged, and if the variable ones continue in the\nlong run to balance one another, the results will continue to\ncluster about the same mean. But if the constant ones\nundergo a gradual change, or if the variable ones, instead of\nbalancing each other suffer one or more of their number to\nbegin to acquire a preponderating influence, so as to put a\nsort of bias upon their aggregate effect, the mean will at\nonce begin, so to say, to shift its ground. And having once\nbegun to shift, it may continue to do so, to whatever extent\nwe recognize that Species are variable and Development is a\nfact. It is as if the point on the target at which we aim, instead\nof being fixed, were slowly changing its position as we\ncontinue to fire at it; changing almost certainly to some extent\nand temporarily, and not improbably to a considerable\nextent and permanently.\n\n20. Our examples throughout this chapter have been\nalmost exclusively drawn from physical characteristics,\nwhether of man or of inanimate things; but it need not be\nsupposed that we are necessarily confined to such instances.\nMr Galton, for instance, has proposed to extend the same\nprinciples of calculation to mental phenomena, with a view\nto their more accurate determination. The objects to be\ngained by so doing belong rather to the inferential part of\nour subject, and will be better indicated further on; but\nthey do not involve any distinct principle. Like other attempts\nto apply the methods of science in the region of the\nmind, this proposal has met with some opposition; with very\nslight reason, as it seems to me. That our mental qualities,\nif they could be submitted to accurate measurement, would\nbe found to follow the usual Law of Error, may be assumed\nwithout much hesitation. The known extent of the correlation\nof mental and bodily characteristics gives high probability\nto the supposition that what is proved to prevail, at\nany rate approximately, amongst most bodily elements which\nhave been submitted to measurement, will prevail also\namongst the mental elements.\n\nTo what extent such measurements could be carried\nout practically, is another matter. It does not seem to\nme that it could be done with much success; partly because\nour mental qualities are so closely connected with,\nindeed so run into one another, that it is impossible to\nisolate them for purposes of comparison.[16] This is to some\nextent indeed a difficulty in bodily measurements, but it is\nfar more so in those of the mind, where we can hardly get\nbeyond what can be called a good guess. The doctrine,\ntherefore, that mental qualities follow the now familiar law\nof arrangement can scarcely be grounded upon anything\nmore than a strong analogy. Still this analogy is quite\nstrong enough to justify us in accepting the doctrine and\nall the conclusions which follow from it, in so far as our\nestimates and measurements can be regarded as trustworthy.\nThere seems therefore nothing unreasonable in the attempt\nto establish a system of natural classification of mankind\nby arranging them into a certain number of groups above\nand below the average, each group being intended to correspond\nto certain limits of excellency or deficiency.[17] All\nthat is necessary for such a purpose is that the rate of\ndeparture from the mean should be tolerably constant under\nwidely different circumstances: in this case throughout all\nthe races of man. Of course if the law of divergence is\nthe same as that which prevails in inanimate nature we\nhave a still wider and more natural system of classification\nat hand, and one which ought to be familiar, more or less, to\nevery one who has thus to estimate qualities.\n\n21. Perhaps one of the best illustrations of the legitimate\napplication of such principles is to be found in Mr\nGalton's work on _Hereditary Genius_. Indeed the full force\nand purport of some of his reasonings there can hardly be\nappreciated except by those who are familiar with the conceptions\nwhich we have been discussing in this chapter. We\ncan only afford space to notice one or two points, but the\nstudent will find in the perusal, of at any rate the more\nargumentive parts, of that volume[18] an interesting illustration\nof the doctrines now under discussion. For one thing it\nmay be safely asserted, that no one unfamiliar with the Law\nof Error would ever in the least appreciate the excessive\nrapidity with which the superior degrees of excellence tend\nto become scarce. Every one, of course, can see at once, in\na numerical way at least, what is involved in being 'one of a\nmillion'; but they would not at all understand, how very\nlittle extra superiority is to be looked for in the man who is\n'one of two million'. They would confound the mere numerical\ndistinction, which seems in some way to imply\ndouble excellence, with the intrinsic superiority, which\nwould mostly be represented by a very small fractional advantage.\nTo be 'one of ten million' sounds very grand, but\nif the qualities under consideration could be estimated in\nthemselves without the knowledge of the vastly wider area\nfrom which the selection had been made, and in freedom\ntherefore from any consequent numerical bias, people would\nbe surprised to find what a very slight comparative superiority\nwas, as a rule, thus obtained.\n\n22. The point just mentioned is an important one in\narguments from statistics. If, for instance, we find a small\ngroup of persons, connected together by blood-relationship,\nand all possessing some mental characteristic in marked\nsuperiority, much depends upon the comparative rarity of\nsuch excellence when we are endeavouring to decide whether\nor not the common possession of these qualities was accidental.\nSuch a decision can never be more than a rough\none, but if it is to be made at all this consideration must\nenter as a factor. Again, when we are comparing one nation\nwith another,[19] say the Athenian with any modern European\npeople, does the popular mind at all appreciate what sort of\nevidence of general superiority is implied by the production,\nout of one nation, of such a group as can be composed of\nSocrates, Plato, and a few of their contemporaries? In this\nlatter case we are also, it should be remarked, employing the\n'Law of Error' in a second way; for we are assuming that\nwhere the extremes are great so will also the means be, in\nother words we are assuming that every amount of departure\nfrom the mean occurs with a (roughly) calculable degree\nof relative frequency. However generally this truth may\nbe accepted in a vague way, its evidence can only be appreciated\nby those who know the reasons which can be given\nin its favour.\n\nBut the same principles will also supply a caution in\nthe case of the last example. They remind us that, for\nthe mere purpose of comparison, the _average_ man of any\ngroup or class is a much better object for selection than\nthe eminent one. There may be greater difficulties in the\nway of detecting him, but when we have done so we have\ngot possession of a securer and more stable basis of comparison.\nHe is selected, by the nature of the case, from\nthe most numerous stratum of his society; the eminent\nman from a thinly occupied stratum. In accordance therefore\nwith the now familiar laws of averages and of large\nnumbers the fluctuations amongst the former will generally\nbe very few and small in comparison with those amongst the\nlatter.\n\n\n1. _Essai de Physique Sociale_, 1869. _Anthropom\u00e9trie_, 1870.\n\n2. As regards later statistics on the same subject the reader can\n  refer to the Reports of the Anthropometrical Committee of the\n  British Association (1879, 1880, 1881, 1883;--especially this\n  last). These reports seem to me to represent a great advance on the\n  results obtained by Quetelet, and fully to justify the claim of the\n  Secretary (Mr C. Roberts) that their statistics are \"unique in range\n  and numbers\". They embrace not merely military recruits--like most\n  of the previous tables--but almost every class and age, and both\n  sexes. Moreover they refer not only to stature but to a number of\n  other physical characteristics.\n\n3. As every mathematician knows, the relative numbers of each of these\n  possible throws are given by the successive terms of the expansion\n  of (1 + 1)^{10}, viz. 1, 10, 45, 120, 210, 252, 210, 120, 45, 10, 1.\n\n4. That is they will be more densely aggregated. If a space _the size\n  of the bull's-eye_ be examined in each successive circle, the number\n  of shot marks which it contains will be successively less. The\n  _actual_ number of shots which strike the bull's-eye will not be the\n  greatest, since it covers so much less surface than any of the other\n  circles.\n\n5. Commonly called the exponential law; its equation being of the form\n  y = Ae^{-hx^{2}}. The curve corresponding to it cuts the axis of y\n  at right angles (expressing the fact that near the mean there are a\n  large number of values approximately equal); after a time it begins\n  to slope away rapidly towards the axis of x (expressing the fact\n  that the results soon begin to grow less common as we recede from\n  the mean); and the axis of x is an asymptote in both directions\n  (expressing the fact that no magnitude, however remote from the\n  mean, is strictly impossible; that is, every deviation, however\n  excessive, will have to be encountered at length within the range of\n  a sufficiently long experience). The curve is obviously symmetrical,\n  expressing the fact that equal deviations from the mean, in excess\n  and in defect, tend to occur equally often in the long run.\n\n  [Figure: Gaussian normal distribution.]\n\n  A rough graphic representation of the curve is given above. For the\n  benefit of those unfamiliar with mathematics one or two brief\n  remarks may be here appended concerning some of its properties.\n  (1) It must not be supposed that all specimens of the curve are\n  similar to one another. The dotted lines are equally specimens of\n  it. In fact, by varying the essentially arbitrary units in which x\n  and y are respectively estimated, we may make the portion towards\n  the vertex of the curve as obtuse or as acute as we please. This\n  consideration is of importance; for it reminds us that, by varying\n  one of these arbitrary units, we could get an 'exponential curve'\n  which should tolerably closely resemble any symmetrical curve of\n  error, provided that this latter recognized and was founded upon the\n  assumption that extreme divergences were excessively rare. Hence it\n  would be difficult, by mere observation, to prove that the law of\n  error in any given case was not exponential; unless the statistics\n  were very extensive, or the actual results departed considerably\n  from the exponential form. (2) It is quite impossible by any graphic\n  representation to give an adequate idea of the excessive rapidity\n  with which the curve after a time approaches the axis of x. At the\n  point R, on our scale, the curve would approach within the\n  fifteen-thousandth part of an inch from the axis of x, a distance\n  which only a very good microscope could detect. Whereas in the\n  hyperbola, e.g. the rate of approach of the curve to its asymptote\n  is continually decreasing, it is here just the reverse; this rate is\n  continually increasing. Hence the two, viz. the curve and the axis\n  of x, appear to the eye, after a very short time, to merge into one\n  another.\n\n6. As by Quetelet: noted, amongst others, by Herschel, _Essays_, page\n  409.\n\n7. _Proc. R. Soc._ Oct. 21, 1879.\n\n8. We are here considering, remember, the case of a _finite_ amount of\n  statistics; so that there are actual limits at each end.\n\n9. It must be admitted that experience has not yet (I believe) shown\n  this asymmetry in respect of heights.\n\n10. The above reasoning will probably be accepted as valid at this\n  stage of enquiry. But in strictness, assumptions are made here,\n  which however justifiable they may be in themselves, involve\n  somewhat of an anticipation. They demand, and in a future chapter\n  will receive, closer scrutiny and criticism.\n\n11. A definite numerical example of this kind of concentration of\n  frequency about the mean was given in the note to \u00a74. It was of a\n  binomial form, consisting of the successive terms of the expansion\n  of (1 + 1)^{m}. Now it may be shown (Quetelet, _Letters_, p. 263;\n  Liagre, _Calcul des Probabilit\u00e9s_, \u00a734) that the expansion of such\n  a binomial, as m becomes indefinitely great, approaches as its limit\n  the exponential form; that is, if we take a number of equidistant\n  ordinates proportional respectively to 1, m, m(m - 1)/(1\u00b72) &c., and\n  connect their vertices, the figure we obtain approximately\n  represents some form of the curve y = Ae^{-hx^{2}}, and tends to\n  become identical with it, as m is increased without limit. In other\n  words, if we suppose the errors to be produced by a limited number\n  of finite, equal and independent causes, we have an approximation to\n  the exponential Law of Error, which merges into identity as the\n  causes are increased in number and diminished in magnitude without\n  limit. Jevons has given (_Principles of Science_, p. 381) a diagram\n  drawn to scale, to show how rapid this approximation is. One point\n  must be carefully remembered here, as it is frequently overlooked\n  (by Quetelet, for instance). The coefficients of a binomial of two\n  equal terms--as (1 + 1)^{m}, in the preceding paragraph--are\n  symmetrical in their arrangement from the first, and very speedily\n  become indistinguishable in (graphical) outline from the final\n  exponential form. But if, on the other hand, we were to consider the\n  successive terms of such a binomial as (1 + 4)^{m} (which are\n  proportional to the relative chances of 0, 1, 2, 3, ... failures in\n  m ventures, of an event which has one chance in its favour to four\n  against it) we should have an unsymmetrical succession. If however\n  we suppose m to increase without limit, as in the former\n  supposition, the unsymmetry gradually disappears and we tend towards\n  precisely the same exponential form as if we had begun with two\n  equal terms. The only difference is that the position of the vertex\n  of the curve is no longer in the centre: in other words, the\n  likeliest term or event is not an equal number of successes and\n  failures but successes and failures in the ratio of 1 to 4.\n\n12. 'Law of Error' is the usual technical term for what has been\n  elsewhere spoken of above as a Law of Divergence from a mean. It is\n  in strictness only appropriate in the case of one, namely the third,\n  of the three classes of phenomena mentioned in \u00a74, but by a\n  convenient generalization it is equally applied to the other two; so\n  that we term the amount of the divergence from the mean an 'error'\n  in every case, however it may have been brought about.\n\n13. This however seems to be the purport, either by direct assertion\n  or by implication, of two elaborate works by Quetelet, viz. his\n  _Physique Sociale_ and his _Anthropom\u00e9trie_.\n\n14. He scarcely, however, professes to give these as an accurate\n  measure of the mean height, nor does he always give precisely the\n  same measure. Practically, none but soldiers being measured in any\n  great numbers, the English stature did not afford accurate data on\n  any large scale. The statistics given a few pages further on are\n  probably far more trustworthy.\n\n15. This statement will receive some explanation and correction in the\n  next chapter.\n\n16. I am not speaking here of the now familiar results of\n  Psychophysics, which are mainly occupied with the measurement of\n  perceptions and other simple states of consciousness.\n\n17. Perhaps the best brief account of Mr Galton's method is to be\n  found in a paper in _Mind_ (July, 1880) on the statistics of Mental\n  Imagery. The subject under comparison here--viz. the relative\n  power, possessed by different persons, of raising clear visual\n  images of objects no longer present to us--is one which it seems\n  impossible to 'measure', in the ordinary sense of the term. But by\n  arranging all the answers in the order in which the faculty in\n  question seems to be possessed we can, with some approach to\n  accuracy, select the middlemost person in the row and use him as a\n  basis of comparison with the corresponding person in any other\n  batch. And similarly with those who occupy other relative positions\n  than that of the middlemost.\n\n18. I refer to the introductory and concluding chapters: the bulk of\n  the book is, from the nature of the case, mainly occupied with\n  statistical and biographical details.\n\n19. See Galton's _Hereditary Genius_, pp. 336-350, \"On the comparative\n  worth of different races.\"\n\n\n\n\nCHAPTER III.\n\n\n_ON THE CAUSAL PROCESS BY WHICH THE GROUPS OR SERIES OF PROBABILITY ARE\nBROUGHT ABOUT._\n\n1. In discussing the question whether all the various\ngroups and series with which Probability is concerned are of\nprecisely one and the same type, we made some examination\nof the process by which they are naturally produced, but we\nmust now enter a little more into the details of this process.\nAll events are the results of numerous and complicated\nantecedents, far too numerous and complicated\nin fact for it to be possible for us to determine or take\nthem all into account. Now, though it is strictly true that\nwe can never determine them all, there is a broad distinction\nbetween the case of Induction, in which we can\nmake out enough of them, and with sufficient accuracy, to\nsatisfy a reasonable certainty, and Probability, in which we\ncannot do so. To Induction we shall return in a future\nchapter, and therefore no more need be said about it here.\n\nWe shall find it convenient to begin with a division\nwhich, though not pretending to any philosophical accuracy,\nwill serve as a preliminary guide. It is the simple division\ninto objects, and the agencies which affect them. All the\nphenomena with which Probability is concerned (as indeed\nmost of those with which science of any kind is concerned)\nare the product of certain objects natural and artificial,\nacting under the influence of certain agencies natural and\nartificial. In the tossing of a penny, for instance, the objects\nwould be the penny or pence which were successively\nthrown; the agencies would be the act of throwing, and\neverything which combined directly or indirectly with this\nto make any particular face come uppermost. This is a\nsimple and intelligible division, and can easily be so extended\nin meaning as to embrace every class of objects with\nwhich we are concerned.\n\nNow if, in any two or more cases, we had the same\nobject, or objects indistinguishably alike, and if they were\nexposed to the influence of agencies in all respects precisely\nalike, we should expect the results to be precisely similar.\nBy one of the applications of the familiar principle of the\nuniformity of nature we should be confident that exact\nlikeness in the antecedents would be followed by exact\nlikeness in the consequents. If the same penny, or similar\npence, were thrown in exactly the same way, we should\ninvariably find that the same face falls uppermost.\n\n2. What we actually find is, of course, very far removed\nfrom this. In the case of the objects, when they\nare artificial constructions, e.g. dice, pence, cards, it is true\nthat they are purposely made as nearly as possible indistinguishably\nalike. We either use the same thing over and\nover again or different ones made according to precisely\nthe same model. But in natural objects nothing of the\nsort prevails. In fact when we come to examine them, we\nfind reproduced in them precisely the same characteristics\nas those which present themselves in the final result which\nwe were asked to explain, so that unless we examine them\na stage further back, as we shall have to do to some extent\nat any rate, we seem to be merely postulating again the\nvery peculiarity of the phenomena which we were undertaking\nto explain. They will be found, for instance, to\nconsist of large classes of objects, throughout all the individual\nmembers of which a general resemblance extends.\nSuppose that we were considering the length of life. The\nobjects here are the human beings, or that selected class\nof them, whose lives we are considering. The resemblance\nexisting among them is to be found in the strength and\nsoundness of their principal vital organs, together with all\nthe circumstances which collectively make up what we call\nthe goodness of their constitutions. It is true that most of\nthese circumstances do not admit of any approach to actual\nmeasurement; but, as was pointed out in the last chapter,\nvery many of the circumstances which do admit of such\nmeasurement have been measured, and found to display\nthe characteristics in question. Hence, from the known\nanalogy and correlation between our various organs, there\ncan be no reasonable doubt that if we could arrange human\nconstitutions in general, or the various elements which compose\nthem in particular, in the order of their strength, we\nshould find just such an aggregate regularity and just such\ngroupings about the mean, as the final result (viz. in this\ncase the length of their lives) presents to our notice.\n\n3. It will be observed therefore that for this purpose\nthe existence of natural kinds or groups is necessary.\nIn our games of chance of course the same die may be\nthrown, or a card be drawn from the same pack, as often\nas we please; but many of the events which occur to\nhuman beings either cannot be repeated at all, or not often\nenough to secure in the case of the single individual any\nsufficient statistical uniformity. Such regularity as we trace\nin nature is owing, much more than is often suspected,\nto the arrangement of things in natural kinds, each of\nthem containing a large number of individuals. Were each\nkind of animals or vegetables limited to a single pair, or\neven to but a few pairs, there would not be much scope\nleft for the collection of statistical tables amongst them.\nOr to take a less violent supposition, if the numbers\nin each natural class of objects were much smaller than\nthey are at present, or the differences between their varieties\nand sub-species much more marked, the consequent\ndifficulty of extracting from them any sufficient length of\nstatistical tables, though not fatal, might be very serious.\nA large number of objects in the class, together with that\ngeneral similarity which entitles the objects to be fairly\ncomprised in one class, seem to be important conditions\nfor the applicability of the theory of Probability to any\nphenomenon. Something analogous to this excessive paucity\nof objects in a class would be found in the attempt to\napply special Insurance offices to the case of those trades\nwhere the numbers are very limited, and the employment\nso dangerous as to put them in a class by themselves. If\nan insurance society were started for the workmen in\ngunpowder mills alone, a premium would have to be charged\nto avoid possible ruin, so high as to illustrate the extreme\npaucity of appropriate statistics.\n\n4. So much (at present) for the objects. If we turn\nto what we have termed the agencies, we find much the\nsame thing again here. By the adjustment of their relative\nintensity, and the respective frequency of their occurrence,\nthe total effects which they produce are found to be also\ntolerably uniform. It is of course conceivable that this\nshould have been otherwise. It might have been found\nthat the second group of conditions so exactly corrected the\nformer as to convert the merely general uniformity into\nan absolute one; or it might have been found, on the\nother hand, that the second group should aggravate or\ndisturb the influence of the former to such an extent\nas to destroy all the uniformity of its effects. Practically\nneither is the case. The second condition simply varies the\ndetails, leaving the uniformity on the whole of precisely\nthe same general description as it was before. Or if the\nobjects were supposed to be absolutely alike, as in the case\nof successive throws of a penny, it may serve to bring about\na uniformity. Analysis will show these agencies to be\nthus made up of an almost infinite number of different\ncomponents, but it will detect the same peculiarity that\nwe have so often had occasion to refer to, pervading almost\nall these components. The proportions in which they are\ncombined will be found to be nearly, though not quite, the\nsame; the intensity with which they act will be nearly\nthough not quite equal. And they will all unite and blend\ninto a more and more perfect regularity as we proceed to\ntake the average of a larger number of instances.\n\nTake, for instance, the length of life. As we have seen,\nthe constitutions of a very large number of persons selected\nat random will be found to present much the same feature;\ngeneral uniformity accompanied by individual irregularity.\nNow when these persons go out into the world, they are\nexposed to a variety of agencies, the collective influence\nof which will assign to each the length of life allotted to\nhim. These agencies are of course innumerable, and their\nmutual interaction complicated beyond all power of analysis\nto extricate. Each effect becomes in its turn a cause, is\ninterwoven inextricably with an indefinite number of other\ncauses, and reacts upon the final result. Climate, food,\nclothing, are some of these agencies, or rather comprise\naggregate groups of them. The nature of a man's work\nis also important. One man overworks himself, another\nfollows an unhealthy trade, a third exposes himself to infection,\nand so on.\n\nThe result of all this interaction between what we have\nthus called objects and agencies is that the final outcome\npresents the same general characteristics of uniformity as may\nbe detected separately in the two constituent elements. Or\nrather, as we shall proceed presently to show, it does so\nin the great majority of cases.\n\n5. It may be objected that such an explanation as\nthe above does not really amount to anything deserving\nof the name, for that instead of explaining how a particular\nstate of things is caused it merely points out that the\nsame state exists elsewhere. There is a uniformity discovered\nin the objects at the stage when they are commonly\nsubmitted to calculation; we then grope about\namongst the causes of them, and after all only discover\na precisely similar uniformity existing amongst these causes.\nThis is to some extent true, for though part of the objection\ncan be removed, it must always remain the case that the\nfoundations of an objective science will rest in the last resort\nupon the mere fact that things are found to be of such and\nsuch a character.\n\n6. This division, into objects and the agencies which\naffect them, is merely intended for a rough practical arrangement,\nsufficient to point out to the reader the immediate\nnature of the causes which bring about our familiar\nuniformities. If we go back a step further, it might fairly\nbe maintained that they may be reduced to one, namely,\nto the agencies. The objects, as we have termed them,\nare not an original creation in the state in which we now\nfind them. No one supposes that whole groups or classes\nwere brought into existence simultaneously, with all their\ngeneral resemblances and particular differences fully developed.\nEven if it were the case that the first parents\nof each natural kind had been specially created, instead\nof being developed out of pre-existing forms, it would still\nbe true that amongst the numbers of each that now present\nthemselves the characteristic differences and resemblances\nare the result of what we have termed agencies. Take, for\ninstance, a single characteristic only, say the height; what\ndetermines this as we find it in any given group of men?\nPartly, no doubt, the nature of their own food, clothing,\nemployment, and so on, especially in the earliest years of\ntheir life; partly also, very likely, similar conditions and\ncircumstances on the part of their parents at one time or\nanother. No one, I presume, in the present state of knowledge,\nwould attempt to enumerate the remaining causes,\nor even to give any indication of their exact nature; but\nat the same time few would entertain any doubt that\nagencies of this general description have been the determining\ncauses at work.\n\nIf it be asked again, Into what may these agencies\nthemselves be ultimately analysed? the answer to this\nquestion, in so far as it involves any detailed examination\nof them, would be foreign to the plan of this essay. In so\nfar as any general remarks, applicable to nearly all classes\nalike of such agencies, are called for, we are led back to\nthe point from which we started in the previous chapter,\nwhen we were discussing whether there is necessarily one\nfixed law according to which all our series are formed. We\nthere saw that every event might be regarded as being\nbrought about by a comparatively few important causes, of\nthe kind which comprises all of which ordinary observation\ntakes any notice, and an indefinitely numerous group of\nsmall causes, too numerous, minute, and uncertain in their\naction for us to be able to estimate them or indeed to take\nthem individually into account at all. The important ones,\nit is true, may also in turn be themselves conceived to be\nmade up of aggregates of small components, but they are\nstill best regarded as being by comparison simple and distinct,\nfor their component parts act mostly in groups collectively,\nappearing and disappearing together, so that they\npossess the essential characteristics of unity.\n\n7. Now, broadly speaking, it appears to me that the\nmost suitable conditions for Probability are these: that the\nimportant causes should be by comparison fixed and permanent,\nand that the remaining ones should on the average\ncontinue to act as often in one direction as in the other.\nThis they may do in two ways. In the first place we\nmay be able to predicate nothing more of them than the\nmere fact that they act[1] as often in one direction as the\nother; what we should then obtain would be merely the\nsimple statistical uniformity that is described in the first\nchapter. But it may be the case, and in practice generally\nis so more or less approximately, that these minor causes\nact also in independence of one another. What we then\nget is a group of uniformities such as was explained and\nillustrated in the second chapter. Every possible combination\nof these causes then occurring with a regular degree\nof frequency, we find one peculiar kind of uniformity\nexhibited, not merely in the mere fact of excess and defect\n(of whatever may be the variable quality in question), but\nalso in every particular amount of excess and defect.\nHence, in this case, we get what some writers term a\n'mean' or 'type,' instead of a simple average. For instance,\nsuppose a man throwing a quoit at a mark. Here\nour fixed causes are his strength, the weight of the quoit,\nand the intention of aiming at a given point. These we\nmust of course suppose to remain unchanged, if we are\nto obtain any such uniformity as we are seeking. The\nminor and variable causes are all those innumerable little\ndisturbing influences referred to in the last chapter. It\nmight conceivably be the case that we were only able to\nascertain that these acted as often in one direction as in\nthe other; what we should then find was that the quoit\ntended to fall short of the mark as often as beyond it.\nBut owing to these little causes being mostly independent\nof one another, and more or less equal in their influence,\nwe find also that every _amount_ of excess and defect presents\nthe same general characteristics, and that in a large number\nof throws the quantity of divergences from the mark, of any\ngiven amount, is a tolerably determinate function, according\nto a regular law, of that amount of divergence.[2]\n\n8. The necessity of the conditions just hinted at\nwill best be seen by a reference to cases in which any of\nthem happen to be missing. Thus we know that the length\nof life is on the whole tolerably regular, and so are the\nnumbers of those who die in successive years or centuries\nof most of the commoner diseases. But it does not seem\nto be the case with all diseases. What, for instance, of\nthe Sweating Sickness, the Black Death, the Asiatic\nCholera? The two former either do not recur, or, if they\ndo, recur in such a mild form as not to deserve the same\nname. What in fact of any of the diseases which are\nepidemic rather than endemic? All these have their causes\ndoubtless, and would be produced again by the recurrence\nof the conditions which caused them before. But some of\nthem apparently do not recur at all. They seem to have\ndepended upon such rare conditions that their occurrence\nwas almost unique. And of those which do recur the course\nis frequently so eccentric and irregular, often so much dependent\nupon human will or want of will, as to entirely\ndeprive their results (that is, the annual number of deaths\nwhich they cause) of the statistical uniformity of which we\nare speaking.\n\nThe explanation probably is that one of the principal\ncauses in such cases is what we commonly call contagion.\nIf so, we have at once a cause which so far from being fixed is\nsubject to the utmost variability. Stringent caution may\ndestroy it, carelessness may aggravate it to any extent. The\nwill of man, as finding its expression either on the part of\ngovernment, of doctors, or of the public, may make of it\npretty nearly what is wished, though against the possibility\nof its entrance into any community no precautions can absolutely\ninsure us.\n\n9. If it be replied that this want of statistical regularity\nonly arises from the fact of our having confined ourselves\nto too limited a time, and that we should find\nirregularity disappear here, as elsewhere, if we kept our\ntables open long enough, we shall find that the answer will\nsuggest another case in which the requisite conditions for\nProbability are wanting. Such a reply would only be conclusive\nupon the supposition that the ways and thoughts of\nmen are in the long run invariable, or if variable, subject to\nperiodic changes only. On the assumption of a steady progress\nin society, either for the better or the worse, the argument\nfalls to the ground at once. From what we know of\nthe course of the world, these fearful pests of the past may\nbe considered as solitary events in our history, or at least\nevents which will not be repeated. No continued uniformity\nwould therefore be found in the deaths which they occasion,\nthough the registrar's books were kept open for a thousand\nyears. The reason here is probably to be sought in the\ngradual alteration of those indefinitely numerous conditions\nwhich we term collectively progress or civilization. Every\nlittle circumstance of this kind has some bearing upon the\nliability of any one to catch a disease. But when a kind of\nslow and steady tide sets in, in consequence of which these\ninfluences no longer remain at about the same average\nstrength, warring on about equal terms with hostile influences,\nbut on the contrary show a steady tendency to increase\ntheir power, the statistics will, with consequent steadiness\nand permanence, take the impress of such a change.\n\n10. Briefly then, if we were asked where the distinctive\ncharacteristics of Probability are most prominently\nto be found, and where they are most prominently absent,\nwe might say that (1) they prevail principally in the properties\nof natural kinds, both in the ultimate and in the derivative\nor accidental properties. In all the characteristics of\nnatural species, in all they do and in all which happens to\nthem, so far as it depends upon their properties, we seldom\nfail to detect this regularity. Thus in men; their height,\nstrength, weight, the age to which they live, the diseases of\nwhich they die; all present a well-known uniformity. Life\ninsurance tables offer the most familiar instance of the importance\nof these applications of Probability.\n\n(2) The same peculiarity prevails again in the force\nand frequency of most natural agencies. Wind and weather\nare seen to lose their proverbial irregularity when examined\non a large scale. Man's work therefore, when operated on\nby such agencies as these, even though it had been made in\ndifferent cases absolutely alike to begin with, afterwards\nshows only a general regularity. I may sow exactly the\nsame amount of seed in my field every year. The yield may\none year be moderate, the next year be abundant through\nfavourable weather, and then again in turn be destroyed by\nhail. But in the long run these irregularities will be equalized\nin the result of my crops, because they are equalized in the\npower and frequency of the productive agencies. The\nbusiness of underwriters, and offices which insure the crops\nagainst hail, would fall under this class; though, as already\nremarked, there is no very profound distinction between them\nand the former class.\n\nThe reader must be reminded again that this fixity is\nonly temporary, that is, that even here the series belong to\nthe class of those which possess a fluctuating type. Those\nindeed who believe in the fixity of natural species will have\nthe best chance of finding a series of the really permanent\ntype amongst them, though even they will admit that some\nchange in the characteristic is attainable in length of time.\nIn the case of the principal natural agencies, it is of course\nincontestable that the present average is referable to the\npresent geological period only. Our average temperature\nand average rainfall have in former times been widely\ndifferent from what they now are, and doubtless will be so again.\n\nAny fuller investigation of the process by which, on the\nTheory of Evolution, out of a primeval simplicity and uniformity\nthe present variety was educed, hardly belongs to\nthe scope of the present work: at most, a few hints must suffice.\n\n11. The above, then, are instances of natural objects\nand natural agencies. There seems reason to believe that it\nis in such things only, as distinguished from things artificial,\nthat the property in question is to be found. This is an assertion\nthat will need some discussion and explanation. Two\ninstances, in apparent opposition, will at once occur to the\nmind of some readers; one of which, from its great intrinsic\nimportance, and the other, from the frequency of the problems\nwhich it furnishes, will demand a few minutes' separate\nexamination.\n\n(1) The first of these is the already mentioned case of\ninstrumental observations. In the use of astronomical and\nother instruments the utmost possible degree of accuracy is\noften desired, a degree which cannot be reasonably hoped for\nin any one single observation. What we do therefore in\nthese cases is to make a large number of successive observations\nwhich are naturally found to differ somewhat from each\nother in their results; by means of these the true value\n(as explained in a future chapter, on the Method of Least\nSquares) is to be determined as accurately as possible. The\nsubjects then of calculation here are a certain number of\nelements, slightly incorrect elements, given by successive\nobservations. Are not these observations artificial, or the\ndirect product of voluntary agency? Certainly not: or rather,\nthe answer depends on what we understand by voluntary.\nWhat is really intended and aimed at by the observer, is of\ncourse, perfect accuracy, that is, the true observation, or the\nvoluntary steps and preliminaries on which this observation\ndepends. Whether voluntary or not, this result only can be\ncalled intentional. But this result is not obtained. What\nwe actually get in its place is a series of deviations from it,\ncontaining results more or less wide of the truth. Now by\nwhat are these deviations caused? By just such agencies as\nwe have been considering in some of the earlier sections in\nthis chapter. Heat and its irregular warping influence,\ndraughts of air producing their corresponding effects, dust\nand consequent friction in one part or another, the slight\ndistortion of the instrument by strains or the slow uneven\ncontraction which continues long after the metal was cast;\nthese and such as these are some of the causes which divert\nus from the truth. Besides this group, there are others\nwhich certainly do depend upon human agency, but which\nare not, strictly speaking, voluntary. They are such as the\nirregular action of the muscles, inability to make our various\norgans and members execute precisely the purposes we have\nin mind, perhaps different rates in the rapidity of the nervous\ncurrents, or in the response to stimuli, in the same or\ndifferent observers. The effect produced by some of these,\nand the allowance that has in consequence to be made, are\nbecoming familiar even to the outside world under the name\nof the 'personal equation' in astronomical, psychophysical,\nand other observations.\n\n12. (2) The other example, alluded to above, is the stock\none of cards and dice. Here, as in the last case, the result\nis remotely voluntary, in the sense that deliberate volition\npresents itself at one stage. But subsequently to this stage,\nthe result is produced or affected by so many involuntary\nagencies that it owes its characteristic properties to these.\nThe turning up, for example, of a particular face of a die is\nthe result of voluntary agency, but it is not an immediate\nresult. That particular face was not chosen, though the fact\nof its being chosen was the remote consequence of an act of\nchoice. There has been an intermediate chaos of conflicting\nagencies, which no one can calculate before or distinguish\nafterwards. These agencies seem to show a uniformity in\nthe long run, and thence to produce a similar uniformity in\nthe result. The drawing of a card from a pack is indeed\nmore directly volitional, as in cutting for partners in a game\nof whist. But no one continues to do this long without\nhaving the pack well shuffled in the interval, whereby a host\nof involuntary influences are let in.\n\n13. The once startling but now familiar uniformities\nexhibited in the cases of suicides and misdirected letters, do\nnot belong to the same class. The final resolution, or want\nof it, which leads to these results, is in each case indeed an\nimportant ingredient in the individual's action or omission;\nbut, in so far as volition has anything to do with the results\n_as a whole_, it instantly disturbs them. If the voice of the\nLegislature speaks out, or any great preacher or moralist\nsucceeds in deterring, or any impressive example in influencing,\nour moral statistics are instantly tampered with.\nSome further discussion will be devoted to this subject in a\nfuture chapter; it need only be remarked here that (always\nexcluding such common or general influence as those just\nmentioned) the average volition, potent as it is in each\nseparate case, is on the whole swayed by non-voluntary conditions,\nsuch as those of health, the casualties of employment, &c.,\nin fact the various circumstances which influence\nthe length of a man's life.\n\n14. Such distinctions as those just insisted on may\nseem to some persons to be needless, but serious errors have\noccasionally arisen from the neglect of them. The immediate\nproducts of man's mind, so far indeed as we can make\nan attempt to obtain them, do not seem to possess this\nessential characteristic of Probability. Their characteristic\nseems rather to be, either perfect mathematical accuracy or\nutter want of it, either law unfailing or mere caprice. If,\ne.g., we find the trees in a forest growing in straight lines,\nwe unhesitatingly conclude that they were planted by man\nas they stand. It is true on the other hand, that if we find\nthem not regularly planted, we cannot conclude that they\nwere not planted by man; partly because the planter may\nhave worked without a plan, partly because the subsequent\nirregularities brought on by nature may have obscured the\nplan. Practically the mind has to work by the aid of imperfect\ninstruments, and is subjected to many hindrances\nthrough various and conflicting agencies, and by these means\nthe work loses its original properties. Suppose, for instance,\nthat a man, instead of producing numerical results by imperfect\nobservations or by the cast of dice, were to select\nthem at first hand for himself by simply thinking of them\nat once; what sort of series would he obtain? It would be\nabout as difficult to obtain in this way any such series as\nthose appropriate to Probability as it would be to keep his\nheart or pulse working regularly by direct acts of volition,\nsupposing that he had the requisite control over these organs.\nBut the mere suggestion is absurd. A man must have an\nobject in thinking, he must think according to a rule or formula;\nbut unless he takes some natural series as a copy, he\nwill never be able to construct one mentally which shall permanently\nimitate the originals. Or take another product of\nhuman efforts, in which the intention can be executed with\ntolerable success. When any one builds a house, there are\nmany slight disturbing influences at work, such as shrinking\nof bricks and mortar, settling of foundations, &c. But the\neffect which these disturbances are able to produce is so inappreciably\nsmall, that we may fairly consider that the result\nobtained is the direct product of the mind, the accurate\nrealization of its intention. What is the consequence?\nEvery house in the row, if designed by one man and at one\ntime, is of exactly the same height, width, &c. as its\nneighbours; or if there are variations they are few, definite,\nand regular. The result offers no resemblance whatever to\nthe heights, weights, &c. of a number of men selected at\nrandom. The builder probably had some regular design in\ncontemplation, and he has succeeded in executing it.\n\n15. It may be replied that if we extend our observations,\nsay to the houses of a large city, we shall then detect\nthe property under discussion. The different heights of a\ngreat number, when grouped together, might be found to\nresemble those of a great number of human beings under\nsimilar treatment. Something of this kind might not improbably\nbe found to be the case, though the resemblance\nwould be far from being a close one. But to raise this\nquestion is to get on to different ground, for we were\nspeaking (as remarked above) not of the work of different\nminds with their different aims, but of that of one mind.\nIn a multiplicity of designs, there may be that variable uniformity,\nfor which we may look in vain in a single design.\nThe heights which the _different_ builders contemplated\nmight be found to group themselves into something of the\nsame kind of uniformity as that which prevails in most\nother things which they should undertake to do independently.\nWe might then trace the action of the same two\nconditions,--a uniformity in the multitude of their different\ndesigns, a uniformity also in the infinite variety of the\ninfluences which have modified those designs. But this is a\nvery different thing from saying that the work of one man\nwill show such a result as this. The difference is much like\nthat between the tread of a thousand men who are stepping\nwithout thinking of each other, and their tread when they\nare drilled into a regiment. In the former case there is\nthe working, in one way or another, of a thousand minds;\nin the latter, of one only.\n\nThe investigations of this and the former chapter\nconstitute a sufficiently close examination into the detailed\ncauses by which the peculiar form of statistical results with\nwhich we are concerned is actually produced, to serve the\npurpose of a work which is occupied mainly with the _methods_\nof the Science of Probability. The great importance, however,\nof certain statistical or sociological enquiries will demand\na recurrence in a future chapter to one particular\napplication of these statistics, viz. to those concerned with\nsome classes of human actions.\n\n16. The only important addition to, or modification of,\nthe foregoing remarks which I have found occasion to make\nis due to Mr Galton. He has recently pointed out,--and was\nI believe the first to do so,--that in certain cases some\nanalysis of the causal processes can be effected, and is in fact\nabsolutely necessary in order to account for the facts observed.\nTake, for instance, the _heights_ of the population of\nany country. If the distribution or dispersion of these about\ntheir mean value were left to the unimpeded action of those\nmyriad productive agencies alluded to above, we should certainly\nobtain such an arrangement in the posterity of any\none generation as had already been exhibited in the parents.\nThat is, we should find repeated in the previous stage the\nsame kind of order as we were trying to account for in the\nfollowing stage.\n\nBut then, as Mr Galton insists, if such agencies acted\nfreely and independently, though we should get the same\n_kind_ of arrangement or distribution, we should not get the\nsame _degree_ of it: there would, on the contrary, be a tendency\ntowards further dispersion. The 'curve of facility' (v. the\ndiagram on p. 29) would belong to the same class, but would\nhave a different modulus. We shall see this at once if we\ntake for comparison a case in which similar agencies work\ntheir way without any counteraction whatever. Suppose, for\ninstance, that a large number of persons, whose fortunes\nwere equal to begin with, were to commence gambling or\nbetting continually for some small sum. If we examine\ntheir circumstances after successive intervals of time, we\nshould expect to find their fortunes distributed according to\nthe same general law,--i.e. the now familiar law in question,--but\nwe should also expect to find that the poorest\nones were slightly poorer, and the richest ones slightly\nricher, on each successive occasion. We shall see more\nabout this in a future chapter (on _Gambling_), but it may\nbe taken for granted here that there is nothing in the laws\nof chance to resist this tendency towards intensifying the extremes.\n\nNow it is found, on the contrary, in the case of vital\nphenomena,--for instance in that of height, and presumably\nof most of the other qualities which are in any way characteristic\nof natural kinds,--that there is, through a number of\nsuccessive generations, a remarkable degree of fixity. The\ntall men are not taller, and the short men are not shorter,\nper cent. of the population in successive generations: always\nsupposing of course that some general change of circumstances,\nsuch as climate, diet, &c. has not set in. There\nmust therefore here be some cause at work which tends, so\nto say, to draw in the extremes and thus to check the otherwise\ncontinually increasing dispersion.\n\n17. The facts were first tested by careful experiment.\nAt the date of Mr Galton's original paper on the subject,[3]\nthere were no available statistics of heights of human beings;\nso a physical element admitting of careful experiment (viz.\nthe size or weight of certain seeds) was accurately estimated.\nFrom these data the actual amount of reversion from the\nextremes, that is, of the slight pressure continually put upon\nthe extreme members with the result of crowding them back\ntowards the mean, was determined, and this was compared\nwith what theory would require in order to keep the characteristics\nof the species permanently fixed. Since then,\nstatistics have been obtained to a large extent which deal\ndirectly with the heights of human beings.\n\nThe general conclusion at which we arrive is that there\nare several causes at work which are neither slight nor independent.\nThere is, for instance, the observed fact that the\nextremes are as a rule not equally fertile with the means,\nnor equally capable of resisting death and disease. Hence\nas regards their mere numbers, there is a tendency for them\nsomewhat to thin out. Then again there is a distinct\npositive cause in respect of 'reversion.' Not only are the\noffspring of the extremes less numerous, but these offspring\nalso tend to cluster about a mean which is, so to say, shifted\na little towards the true centre of the whole group; i.e. towards\nthe mean offspring of the mean parents.\n\n18. For a full discussion of these characteristics, and\nfor a variety of most ingenious illustrations of their mode of\nagency and of their comparative efficacy, the reader may be\nreferred to Mr Galton's original articles. For our present\npurpose it will suffice to say that these characteristics tend\ntowards maintaining the fixity of species; and that though\nthey do not affect what may be called the general nature of\nthe 'probability curve' or 'law of facility', they do determine\nits precise value in the cases in question. If, indeed, it be\nasked why there is no need for any such corrective influence\nin the case of, say, firing at a mark: the answer is that there\nis no opening for it except where a _cumulative_ influence is introduced.\nThe reason why the fortunes of our betting party\nshowed an ever increasing divergency, and why some special\ncorrection was needed in order to avert such a tendency in\nthe case of vital phenomena, was that the new starting-point\nat every step was slightly determined by the results of the\nprevious step. The man who has lost a shilling one time\nstarts, next time, worse off by just a shilling; and, but for\nthe corrections we have been indicating, the man who was\nborn tall would, so to say, throw off his descendants from a\nvantage ground of superior height. The true parallel in the\ncase of the marksmen would be to suppose that their new\npoints of aim were always shifted a little in the direction of\nthe last divergence. The spreading out of the shot-marks\nwould then continue without limit, just as would the divergence\nof fortunes of the supposed gamblers.\n\n\n1. As stated above, this is really little more than a re-statement, a\n  stage further back, of the existence of the same kind of uniformity\n  as that which we are called upon to explain in the concrete details\n  presented to us in experience.\n\n2. \"It would seem in fact that in coarse and rude observations the\n  errors proceed from a _very few_ principal causes, and in\n  consequence our hypothesis [as to the Exponential Law of Error] will\n  probably represent the facts only imperfectly, and the frequency of\n  the errors will only approximate roughly and vaguely to the law\n  which follows from it. But when astronomers, not content with the\n  degree of accuracy they had reached, prosecuted their researches\n  into the remaining sources of error, they found that not three or\n  four, but a _great number_ of minor sources of error of nearly\n  co-ordinate importance began to reveal themselves, having been till\n  then masked and overshadowed by the graver errors which had been now\n  approximately removed.... There were errors of graduation, and many\n  others in the contraction of instruments; other errors of their\n  adjustments; errors (technically so called) of _observation_; errors\n  from the changes of temperature, of weather, from slight irregular\n  motions and vibrations; in short, the thousand minute disturbing\n  influences with which modern astronomers are familiar.\" (Extracted\n  from a paper by Mr Crofton in the Vol. of the _Philosophical\n  Transactions_ for 1870, p. 177.)\n\n3. _Typical Laws of Heredity_; read before the Royal Institution,\n  Feb. 9, 1877. See also _Journal of the Anthrop. Inst._ Nov. 1885.\n\n\n\n\nCHAPTER IV.\n\n\n_ON THE MODES OF ESTABLISHING AND DETERMINING THE EXISTENCE AND\nNUMERICAL PROPORTIONS OF THE CHARACTERISTIC PROPERTIES OF OUR SERIES\nOR GROUPS._\n\n1. At the point which we have now reached, we are\nsupposed to be in possession of series or groups of a certain\nkind, lying at the bottom, as one may say, and forming the\nfoundation on which the Science of Probability is to be\nerected. We have described with sufficient particularity the\ncharacteristics of such a series, and have indicated the process\nby which it is, as a rule, actually brought about in\nnature. The next enquiries which have to be successively\nmade are, how in any particular case we are to establish\ntheir existence and determine their special character and\nproperties? and secondly,[1] when we have obtained them, in\nwhat mode are they to be employed for logical purposes?\n\nThe answer to the former enquiry does not seem difficult.\nExperience is our sole guide. If we want to discover what is\nin reality a series of _things_, not a series of our own conceptions,\nwe must appeal to the things themselves to obtain it,\nfor we cannot find much help elsewhere. We cannot tell\nhow many persons will be born or die in a year, or how\nmany houses will be burnt or ships wrecked, without actually\ncounting them. When we thus speak of 'experience' we\nmean to employ the term in its widest signification; we\nmean experience supplemented by all the aids which inductive\nor deductive logic can afford. When, for instance,\nwe have found the series which comprises the numbers of\npersons of any assigned class who die in successive years, we\nhave no hesitation in extending it some way into the future\nas well as into the past. The justification of such a procedure\nmust be sought in the ordinary canons of Induction.\nAs a special discussion will be given upon the connection\nbetween Probability and Induction, no more need be said\nupon this subject here; but nothing will be found there at\nvariance with the assertion just made, that the series we\nemploy are ultimately obtained by experience only.\n\n2. In many cases it is undoubtedly true that we do not\nresort to direct experience at all. If I want to know what is\nmy chance of holding ten trumps in a game of whist, I do\nnot enquire how often such a thing has occurred before. If\nall the inhabitants of the globe were to divide themselves up\ninto whist parties they would have to keep on at it for a\ngreat many years, if they wanted to settle the question\nsatisfactorily in that way. What we do of course is to calculate\nalgebraically the proportion of possible combinations\nin which ten trumps can occur, and take this as the answer\nto our problem. So again, if I wanted to know the chance\nof throwing six with a die whose faces were unequal, it\nwould be a question if my best way would not be to calculate\ngeometrically the solid angle subtended at the centre of\ngravity by the opposite face, and the ratio of this to the\nwhole surface of a sphere would represent sufficiently closely\nthe chance required.\n\nIt is quite true that in such examples as the above, especially\nthe former one, nobody would ever think of appealing\nto statistics. This would be a tedious process to adopt when,\nas here, the mechanical and other conditions upon which the\nproduction of the events depend are comparatively few, determinate,\nand admit of isolated consideration, whilst the\nenormous number of combinations which can be constructed\nout of them causes an enormous consequent multiplicity of\nways in which the events can possibly happen. Hence, in\npractice, _\u00e0 priori_ determination is often easy, whilst _\u00e0 posteriori_\nappeal to experience would be not merely tedious but\nutterly impracticable. This, combined with the frequent\nsimplicity and attractiveness of such examples when deductively\ntreated, has made them very popular, and produced the\nimpression in many quarters that they are the proper typical\ninstances to illustrate the theory of chance. Whereas, had\nthe science been concerned with those kinds of events only\nwhich in practice are commonly made subjects of insurance,\nprobably no other view would ever have been taken than\nthat it was based upon direct appeal to experience.\n\n3. When, however, we look a little closer, we find that\nthere is no occasion for such a sharp distinction as that apparently\nimplied between the two classes of examples just\nindicated. In such cases as those of dice and cards, even, in\nwhich we appear to reason directly from the determining\nconditions, or possible variety of the events, rather than from\nactual observation of their occurrence, we shall find that this\nprocedure is only valid by the help of a tacit assumption\nwhich can never be determined otherwise than by direct\nexperience. It is, no doubt, an exceedingly natural and\nobvious assumption, and one which is continually deriving\nfresh weight from every-day observation, but it is one which\nought not to be admitted without consideration. As this is a\nvery important matter, not so much in itself as in connection\nwith the light which it throws upon the theory of the subject,\nwe will enter into a somewhat detailed examination of it.\n\nLet us take a very simple example, that of tossing up a\npenny. Suppose that I am contemplating a succession of\ntwo throws; I can see that the only possible events are[2]\nHH, HT, TH, TT. So much is certain. We are moreover\ntolerably well convinced from experience that these\nevents occur, in the long run, about equally often. This is\nof course admitted on all hands. But on the view commonly\nmaintained, it is contended that we might have known the\nfact beforehand on grounds which are applicable to an indefinite\nnumber of other and more complex cases. The form in\nwhich this view would generally be advanced is, that we are\nenabled to state beforehand that the four throws above mentioned\nare _equally likely_. If in return we ask what is meant\nby the expression 'equally likely', it appears that there are\ntwo and only two possible forms of reply. One of these seeks\nthe explanation in the state of mind of the observer, the\nother seeks it in some characteristic of the things observed.\n\n(1) It might, for instance, be said on the one hand, that\nwhat is meant is that the four events contemplated are\nequally easy to imagine, or, more accurately, that our expectation\nor belief in their occurrence is equal. We could\nhardly be content with this reply, for the further enquiry\nwould immediately be urged, On what ground is this to be\nbelieved? What are the characteristics of events of which\nour expectation is equal? If we consented to give an answer\nto this further enquiry, we should be led to the second form\nof reply, to be noticed directly; if we did not consent we\nshould, it seems, be admitting that Probability was only a\nportion of Psychology, confined therefore to considering states\nof mind in themselves, rather than in their reference to facts,\nviz. as being true or false. We should, that is, be ceasing\nto make it a science of inference about things. This point\nwill have to be gone into more thoroughly in another chapter;\nbut it is impossible to direct attention too prominently\nto the fact that Logic (and therefore Probability as a branch\nof Logic) is not concerned with what men _do_ believe, but\nwith what they ought to believe, if they are to believe\ncorrectly.\n\n(2) In the other form of reply the explanation of the\nphrase in question would be sought, not in a state of mind,\nbut in a quality of the things contemplated. We might assign\nthe following as the meaning, viz. that the events really\nwould occur with equal frequency in the long run. The\nground of this assertion would probably be found in past experience,\nand it would doubtless be impossible so to frame\nthe answer as to exclude the notion of our belief altogether.\nBut still there is a broad distinction between seeking an\nequality in the amount of our belief, as before, and in the\nfrequency of occurrence of the events themselves, as here.\n\n4. When we have got as far as this it can readily be\nshown that an appeal to experience cannot be long evaded.\nFor _can_ the assertion in question (viz. that the throws of the\npenny will occur equally often) be safely made _\u00e0 priori_?\nThose who consider that it can seem hardly to have fully\nfaced the difficulties which meet them. For when we begin\nto enquire seriously whether the penny will really do what\nis expected of it, we find that restrictions have to be introduced.\nIn the first place it must be an ideal coin, with\nits sides equal and fair. This restriction is perfectly intelligible;\nthe study of solid geometry enables us to idealize a\npenny into a circular or cylindrical lamina. But this condition\nby itself is not sufficient, others are wanted as well. The\npenny was supposed to be tossed up, as we say 'at random.'\nWhat is meant by this, and how is this process to be idealized?\nTo ask this is to introduce no idle subtlety; for it\nwould scarcely be maintained that the heads and tails would\nget their fair chances if, immediately before the throwing,\nwe were so to place the coin in our hands as to start it\nalways with the same side upwards. The difference that\nwould result in consequence, slight as its cause is, would\ntend in time to show itself in the results. Or, if we persisted\nin starting with each of the two sides alternately\nupwards, would the longer repetitions of the same side get\ntheir fair chance?\n\nPerhaps it will be replied that if we think nothing whatever\nabout these matters all will come right of its own accord.\nIt may, and doubtless will be so, but this is falling back upon\nexperience. It is here, then, that we find ourselves resting on\nthe experimental assumption above mentioned, and which\nindeed cannot be avoided. For suppose, lastly, that the\ncircumstances of nature, or my bodily or mental constitution,\nwere such that the same side always _is_ started upwards, or\nindeed that they are started in any arbitrary order of our\nown? Well, it will be replied, it would not then be a fair\ntrial. If we press in this way for an answer to such enquiries,\nwe shall find that these tacit restrictions are really nothing\nelse than a mode of securing an experimental result. They\nare only another way of saying, Let a series of actions be\nperformed in such a way as to secure a sequence of a particular\nkind, viz., of the kind described in the previous chapters.\n\n5. An intermediate way of evading the direct appeal\nto experience is sometimes found by defining the probability\nof an event as being measured by the ratio which the\nnumber of cases favourable to the event bears to the total\nnumber of cases which are possible. This seems a somewhat\nloose and ambiguous way of speaking. It is clearly not\nenough to _count_ the number of cases merely, they must also\nbe _valued_, since it is not certain that each is equally potent\nin producing the effect. This, of course, would never be\ndenied, but sufficient importance does not seem to be attached\nto the fact that we have really no other way of\nvaluing them except by estimating the effects which they\nactually do, or would produce. Instead of thus appealing to\nthe proportion of cases favourable to the event, it is far better\n(at least as regards the foundation of the science, for we are\nnot at this moment discussing the practical method of facilitating\nour calculations) to appeal at once to the proportion\nof cases in which the event actually occurs.\n\n6. The remarks above made will apply, of course, to\nmost of the other common examples of chance; the throwing\nof dice, drawing of cards, of balls from bags, &c. In the\nlast case, for instance, one would naturally be inclined to\nsuppose that a ball which had just been put back would\nthereby have a better chance of coming out again next time,\nsince it will be more in the way for that purpose. How is\nthis to be prevented? If we designedly thrust it to the\nmiddle or bottom of the others, we may overdo the precaution;\nand are in any case introducing human design, that\nelement so essentially hostile to all that we understand by\nchance. If we were to trust to a good shake setting matters\nright, we may easily be deceived; for shaking the bag can\nhardly do more than diminish the disposition of those balls\nwhich were already in each other's neighbourhood, to remain\nso. In the consequent interaction of each upon all, the\narrangement in which they start cannot but leave its impress\nto some extent upon their final positions. In all such cases,\ntherefore, if we scrutinize our language, we shall find that\nany supposed _\u00e0 priori_ mode of stating a problem is little else\nthan a compendious way of saying, Let means be taken for\nobtaining a given result. Since it is upon this result that\nour inferences ultimately rest, it seems simpler and more\nphilosophical to appeal to it at once as the groundwork of\nour science.\n\n7. Let us again take the instance of the tossing of a\npenny, and examine it somewhat more minutely, to see what\ncan be actually proved about the results we shall obtain.\nWe are willing to give the pence fair treatment by assuming\nthat they are perfect, that is, that in the long run they show\nno preference for either head or tail; the question then\nremains, Will the repetitions of the same face obtain the\nproportional shares to which they are entitled by the\nusual interpretations of the theory? Putting then, as before,\nfor the sake of brevity, H for head, and HH for heads twice\nrunning, we are brought to this issue;--Given that the\nchance of H is 1/2, does it follow necessarily that the chance of HH\n(with two pence) is 1/4? To say nothing of 'H ten times'\noccurring once in 1024 times (with ten pence), need it occur\nat all? The mathematicians, for the most part, seem to think\nthat this conclusion follows necessarily from first principles;\nto me it seems to rest upon no more certain evidence than a\nreasonable extension by Induction.\n\nTaking then the possible results which can be obtained\nfrom a pair of pence, what do we find? Four different\nresults may follow, namely, (1) HT, (2) HH, (3) TH, (4) TT.\nIf it can be proved that these four are equally probable, that\nis, occur equally often, the commonly accepted conclusions\nwill follow, for a precisely similar argument would apply to\nall the larger numbers.\n\n8. The proof usually advanced makes use of what is\ncalled the Principle of Sufficient Reason. It takes this\nform;--Here are four kinds of throws which may happen;\nonce admit that the separate elements of them, namely, H\nand T, happen equally often, and it will follow that the above\ncombinations will also happen equally often, for no reason can\nbe given in favour of one of them that would not equally hold\nin favour of the others.\n\nTo a certain extent we must admit the validity of the\nprinciple for the purpose. In the case of the throws given\nabove, it would be valid to prove the equal frequency of (1)\nand (3) and also of (2) and (4); for there is no difference\nexisting between these pairs except what is introduced by our\nown notation.[3] TH is the same as HT, except in the order\nof the occurrence of the symbols H and T, which we do not\ntake into account. But either of the pair (1) and (3) _is_\ndifferent from either of the pair (2) and (4). Transpose the\nnotation, and there would still remain here a distinction which\nthe mind can recognize. A succession of the same thing\ntwice running is distinguished from the conjunction of two\ndifferent things, by a distinction which does not depend\nupon our arbitrary notation only, and would remain entirely\nunaltered by a change in this notation. The principle therefore\nof Sufficient Reason, if admitted, would only prove that\ndoublets of the two kinds, for example (2) and (4), occur\nequally often, but it would not prove that they must each\noccur once in four times. It cannot be proved indeed in this\nway that they need ever occur at all.\n\n9. The formula, then, not being demonstrable _\u00e0 priori_,\n(as might have been concluded,) can it be obtained by experience?\nTo a certain extent it can; the present experience\nof mankind in pence and dice seems to show that the smaller\nsuccessions of throws do really occur in about the proportions\nassigned by the theory. But how nearly they do so no one\ncan say, for the amount of time and trouble to be expended\nbefore we could feel that we have verified the fact, even for\nsmall numbers, is very great, whilst for large numbers it\nwould be simply intolerable. The experiment of throwing\noften enough to obtain 'heads ten times' has been actually\nperformed by two or three persons, and the results are given\nby De Morgan, and Jevons.[4] This, however, being only\nsufficient on the average to give 'heads ten times' a single\nchance, the evidence is very slight; it would take a considerable\nnumber of such experiments to set the matter\nnearly at rest.\n\nAny such rule, then, as that which we have just been\ndiscussing, which professes to describe what will take place\nin a long succession of throws, is only conclusively proved by\nexperience within very narrow limits, that is, for small repetitions\nof the same face; within limits less narrow, indeed,\nwe feel assured that the rule cannot be flagrantly in error,\notherwise the variation would be almost sure to be detected.\nFrom this we feel strongly inclined to infer that the same\nlaw will hold throughout. In other words, we are inclined\nto extend the rule by Induction and Analogy. Still there\nare so many instances in nature of proposed laws which hold\nwithin narrow limits but get egregiously astray when we\nattempt to push them to great lengths, that we must give at\nbest but a qualified assent to the truth of the formula.\n\n10. The object of the above reasoning is simply to\nshow that we cannot be certain that the rule is true. Let\nus now turn for a minute to consider the causes by which\nthe succession of heads and tails is produced, and we may\nperhaps see reasons to make us still more doubtful.\n\nIt has been already pointed out that in calculating probabilities\n_\u00e0 priori_, as it is called, we are only able to do so by\nintroducing restrictions and suppositions which are in reality\nequivalent to assuming the expected results. We use words\nwhich in strictness mean, Let a given process be performed;\nbut an analysis of our language, and an examination of\nvarious tacit suppositions which make themselves felt the\nmoment they are not complied with, soon show that our real\nmeaning is, Let a series of a given kind be obtained; it is to\nthis series only, and not to the conditions of its production,\nthat all our subsequent calculations properly apply. The\nphysical process being performed, we want to know whether\nanything resembling the contemplated series really will be\nobtained.\n\nNow if the penny were invariably set the same side uppermost,\nand thrown with the same velocity of rotation and\nto the same height, &c.--in a word, subjected to the same\nconditions,--it would always come down with the same side\nuppermost. Practically, we know that nothing of this kind\noccurs, for the individual variations in the results of the\nthrows are endless. Still there will be an _average_ of these\nconditions, about which the throws will be found, as it were,\nto cluster much more thickly than elsewhere. We should be\ninclined therefore to infer that if the same side were always\nset uppermost there would really be a departure from the\nsort of series which we ordinarily expect. In a very large\nnumber of throws we should probably begin to find, under\nsuch circumstances, that either head or tail was having a\npreference shown to it. If so, would not similar effects be\nfound to be connected with the way in which we started\neach successive _pair_ of throws? According as we chose to\nmake a practice of putting HH or TT uppermost, might\nthere not be a disturbance in the proportion of successions of\ntwo heads or two tails? Following out this train of reasoning,\nit would seem to point with some likelihood to the conclusion\nthat in order to obtain a series of the kind we\nexpect, we should have to dispose the antecedents in a\nsimilar series at the start. The changes and chances produced\nby the act of throwing might introduce infinite individual\nvariations, and yet there might be found, in the very\nlong run, to be a close similarity between these two series.\n\n11. This is, to a certain extent, only shifting the difficulty,\nI admit; for the claim formerly advanced about the\npossibility of proving the proportions of the throws in the\nformer series, will probably now be repeated in favour of\nthose in the latter. Still the question is very much narrowed,\nfor we have reduced it to a series of _voluntary_ acts.\nA man may put whatever side he pleases uppermost. He\nmay act consciously, as I have said, or he may think nothing\nwhatever about the matter, that is, throw at random; if so,\nit will probably be asserted by many that he will involuntarily\nproduce a series of the kind in question. It may be\nso, or it may not; it does not seem that there are any\neasily accessible data by which to decide. All that I am\nconcerned with here is to show the likelihood that the commonly\nreceived result does in reality depend upon the fulfilment\nof a certain condition at the outset, a condition which\nit is certainly optional with any one to fulfil or not as he\npleases. The short successions doubtless will take care of\nthemselves, owing to the infinite complications produced by\nthe casual variations in throwing; but the long ones may\nsuffer, unless their interest be consciously or unconsciously\nregarded at the outset.\n\n12. The advice, 'Only try long enough, and you will\nsooner or later get any result that is possible,' is plausible,\nbut it rests only on Induction and Analogy; mathematics do\nnot prove it. As has been repeatedly stated, there are two\ndistinct views of the subject. Either we may, on the one\nhand, take a series of symbols, call them heads and tails;\nH, T, &c.; and make the assumption that each of these, and\neach pair of them, and so on, will occur in the long run with\na regulated degree of frequency. We may then calculate\ntheir various combinations, and the consequences that may\nbe drawn from the data assumed. This is a purely algebraical\nprocess; it is infallible; and there is no limit whatever to the\nextent to which it may be carried. This way of looking at\nthe matter may be, and undoubtedly should be, nothing\nmore than the counterpart of what I have called the substituted\nor idealized series which generally has to be introduced\nas the basis of our calculation. The danger to be guarded\nagainst is that of regarding it too purely as an algebraical\nconception, and thence of sinking into the very natural\nerrors both of too readily evolving it out of our own consciousness,\nand too freely pushing it to unwarranted lengths.\n\nOr on the other hand, we may consider that we are treating\nof the behaviour of _things_;--balls, dice, births, deaths, &c.;\nand drawing inferences about them. But, then, what\nwere in the former instance allowable assumptions, become\nhere propositions to be tested by experience. Now the whole\ntheory of Probability as a practical science, in fact as anything\nmore than an algebraical truth, depends of course upon\nthere being a close correspondence between these two views\nof the subject, in other words, upon our substituted series\nbeing kept in accordance with the actual series. Experience\nabundantly proves that, between considerable limits, in the\nexample in question, there does exist such a correspondence.\nBut let no one attempt to enforce our assent to every remote\ndeduction that mathematicians can draw from their formul\u00e6.\nWhen this is attempted the distinction just traced becomes\nprominent and important, and we have to choose our side.\nEither we go over to the mathematics, and so lose all right\nof discussion about the things; or else we take part with the\nthings, and so defy the mathematics. We do not question\nthe formal accuracy of the latter within their own province,\nbut either we dismiss them as somewhat irrelevant, as applying\nto data of whose correctness we cannot be certain, or\nwe take the liberty of remodelling them so as to bring them\ninto accordance with facts.\n\n13. A critic of any doctrine can hardly be considered\nto have done much more than half his duty when he has\nexplained and justified his grounds for objecting to it. It\nstill remains for him to indicate, if only in a few words,\nwhat he considers its legitimate functions and position to be,\nfor it can seldom happen that he regards it as absolutely\nworthless or unmeaning. I should say, then, that when\nProbability is thus divorced from direct reference to objects,\nas it substantially is by not being founded upon experience,\nit simply resolves itself into the common algebraical or arithmetical\ndoctrine of Permutations and Combinations.[5] The\nconsiderations upon which these depend are purely formal\nand necessary, and can be fully reasoned out without any\nappeal to experience. We there start from pure considerations\nof number or magnitude, and we terminate with them,\nhaving only arithmetical calculations to connect them together.\nI wish, for instance, to find the chance of throwing\nheads three times running with a penny. All I have to do\nis first to ascertain the possible number of throws. Permutations\ntell me that with two things thus in question (viz.\nhead and tail) and three times to perform the process, there\nare eight possible forms of the result. Of these eight one\nonly being favourable, the chance in question is pronounced\nto be one-eighth.\n\nNow though it is quite true that the actual calculation of\nevery chance problem must be of the above character, viz. an\nalgebraical or arithmetical process, yet there is, it seems to\nme, a broad and important distinction between a material\nscience which employs mathematics, and a formal one which\nconsists of nothing but mathematics. When we cut ourselves\noff from the necessity of any appeal to experience, we\nare retaining only the intermediate or calculating part of the\ninvestigation; we may talk of dice, or pence, or cards, but\nthese are really only names we choose to give to our symbols.\nThe H's and T's with which we deal have no bearing on objective\noccurrences, but are just like the x's and y's with\nwhich the rest of algebra deals. Probability in fact, when so\ntreated, seems to be absolutely nothing else than a system of\napplied Permutations and Combinations.\n\nIt will now readily be seen how narrow is the range of\ncases to which any purely deductive method of treatment can\napply. It is almost entirely confined to such employments\nas games of chance, and, as already pointed out, can only be\nregarded as really trustworthy even there, by the help of\nvarious tacit restrictions. This alone would be conclusive\nagainst the theory of the subject being rested upon such a\nbasis. The experimental method, on the other hand, is, in the\nsame theoretical sense, of universal application. It would\ninclude the ordinary problems furnished by games of chance,\nas well as those where the dice are loaded and the pence are\nnot perfect, and also the indefinitely numerous applications\nof statistics to the various kinds of social phenomena.\n\n14. The particular view of the deductive character of\nProbability above discussed, could scarcely have intruded\nitself into any other examples than those of the nature of\ngames of chance, in which the conditions of occurrence are\nby comparison few and simple, and are amenable to accurate\nnumerical determination. But a doctrine, which is in reality\nlittle else than the same theory in a slightly disguised form,\nis very prevalent, and has been applied to truths of the most\npurely empirical character. This doctrine will be best introduced\nby a quotation from Laplace. After speaking of\nthe irregularity and uncertainty of nature as it appears at\nfirst sight, he goes on to remark that when we look closer we\nbegin to detect \"a striking regularity which seems to suggest\na design, and which some have considered a proof of\nProvidence. But, on reflection, it is soon perceived that this\nregularity is nothing but the development of the respective\nprobabilities of the simple events, which ought to occur more\nfrequently according as they are more probable.\"[6]\n\nIf this remark had been made about the succession of\nheads and tails in the throwing up of a penny, it would\nhave been intelligible. It would simply mean this: that the\nconstitution of the body was such that we could anticipate\nwith some confidence what the result would be when it was\ntreated in a certain way, and that experience would justify\nour anticipation in the long run. But applied as it is in a\nmore general form to the facts of nature, it seems really to\nhave but little meaning in it. Let us test it by an instance.\nAmidst the irregularity of individual births, we find that the\nmale children are to the female, in the long run, in about\nthe proportion of 106 to 100. Now if we were told that\nthere is nothing in this but \"the development of their respective\nprobabilities,\" would there be anything in such a\nstatement but a somewhat pretentious re-statement of the\nfact already asserted? The probability _is_ nothing but that\nproportion, and is unquestionably in this case derived from\nno other source but the statistics themselves; in the above\nremark the attempt seems to be made to invert this process,\nand to derive the sequence of events from the mere numerical\nstatement of the proportions in which they occur.\n\n15. It will very likely be replied that by the probability\nabove mentioned is meant, not the mere numerical\nproportion between, the births, but some fact in our constitution\nupon which this proportion depends; that just as\nthere was a relation of equality between the two sides of the\npenny, which produced the ultimate equality in the number\nof heads and tails, so there may be something in our constitution\nor circumstances in the proportion of 106 to 100,\nwhich produces the observed statistical result. When this\nsomething, whatever it might be, was discovered, the observed\nnumbers might be supposed capable of being determined\nbeforehand. Even if this were the case, however, it\nmust not be forgotten that there could hardly fail to be, in\ncombination with such causes, other concurrent conditions in\norder to produce the ultimate result; just as besides the shape\nof the penny, we had also to take into account the nature of\nthe 'randomness' with which it was tossed. What these\nmay be, no one at present can undertake to say, for the best\nphysiologists seem indisposed to hazard even a guess upon\nthe subject.[7] But without going into particulars, one may\nassert with some confidence that these conditions cannot well\nbe altogether independent of the health, circumstances, manners\nand customs, &c. (to express oneself in the vaguest way)\nof the parents; and if once these influencing elements are\nintroduced, even as very minute factors, the results cease to\nbe dependent only on fixed and permanent conditions. We\nare at once letting in other conditions, which, if they also\npossess the characteristics that distinguish Probability (an\nexceedingly questionable assumption), must have that fact\nspecially proved about them. That this should be the case\nindeed seems not merely questionable, but almost certainly\nimpossible; for these conditions partaking of the nature of\nwhat we term generally, Progress and Civilization, cannot be\nexpected to show any permanent disposition to hover about\nan average.\n\n16. The reader who is familiar with Probability is of\ncourse acquainted with the celebrated theorem of James\nBernoulli. This theorem, of which the examples just adduced\nare merely particular cases, is generally expressed\nsomewhat as follows:--in the long run all events will tend\nto occur with a relative frequency proportional to their\nobjective probabilities. With the mathematical proof of this\ntheorem we need not trouble ourselves, as it lies outside the\nprovince of this work; but indeed if there is any value in the\nforegoing criticism, the basis on which the mathematics rest\nis faulty, owing to there being really nothing which we can\nwith propriety call an objective probability.\n\nIf one might judge by the interpretation and uses to\nwhich this theorem is sometimes exposed, we should regard\nit as one of the last remaining relics of Realism, which after\nbeing banished elsewhere still manages to linger in the remote\nprovince of Probability. It would be an illustration of\nthe inveterate tendency to objectify our conceptions, even in\ncases where the conceptions had no right to exist at all. A\nuniformity is observed; sometimes, as in games of chance, it\nis found to be so connected with the physical constitution of\nthe bodies employed as to be capable of being inferred beforehand;\nthough even here the connection is by no means\nso necessary as is commonly supposed, owing to the fact that\nin addition to these bodies themselves we have also to take\ninto account their relation to the agencies which influence\nthem. This constitution is then converted into an 'objective\nprobability', supposed to develop into the sequence which\nexhibits the uniformity. Finally, this very questionable objective\nprobability is assumed to exist, with the same faculty\nof development, in all the cases in which uniformity is observed,\nhowever little resemblance there may be between\nthese and games of chance.\n\n17. How utterly inappropriate any such conception is\nin most of the cases in which we find statistical uniformity,\nwill be obvious on a moment's consideration. The observed\nphenomena are generally the product, in these cases, of very\nnumerous and complicated antecedents. The number of\ncrimes, for instance, annually committed in any society, is a\nfunction amongst other things, of the strictness of the law,\nthe morality of the people, their social condition, and the\nvigilance of the police, each of these elements being in itself\nalmost infinitely complex. Now, as a result of all these\nagencies, there is some degree of uniformity; but what has\nbeen called above the change of type, which it sooner or\nlater tends to display, is unmistakeable. The average annual\nnumbers do not show a steady gradual approach towards\nwhat might be considered in some sense a limiting value,\nbut, on the contrary, fluctuate in a way which, however it\nmay depend upon causes, shows none of the permanent uniformity\nwhich is characteristic of games of chance. This\nfact, combined with the obvious arbitrariness of singling out,\nfrom amongst the many and various antecedents which produced\nthe observed regularity, a few only, which should constitute\nthe objective probability (if we took all, the events\nbeing absolutely determined, there would be no occasion for\nan appeal to probability in the case), would have been sufficient\nto prevent any one from assuming the existence of\nany such thing, unless the mistaken analogy of other cases\nhad predisposed him to seek for it.\n\nThere is a familiar practical form of the same error, the\ntendency to which may not improbably be derived from a\nsimilar theoretical source. It is that of continuing to accumulate\nour statistical data to an excessive extent. If the\ntype were absolutely fixed we could not possibly have too\nmany statistics; the longer we chose to take the trouble\nof collecting them the more accurate our results would be.\nBut if the type is changing, in other words, if some of the\nprincipal causes which aid in their production have, in regard\nto their present degree of intensity, strict limits of time or\nspace, we shall do harm rather than good if we overstep\nthese limits. The danger of stopping too soon is easily seen,\nbut in avoiding it we must not fall into the opposite error of\ngoing on too long, and so getting either gradually or suddenly\nunder the influence of a changed set of circumstances.\n\n18. This chapter was intended to be devoted to a\nconsideration, not of the processes by which nature produces\nthe series with which we are concerned, but of the theoretic\nbasis of the methods by which we can determine the existence\nof such series. But it is not possible to keep the two enquiries\napart, for here, at any rate, the old maxim prevails that to\nknow a thing we must know its causes. Recur for a minute\nto the considerations of the last chapter. We there saw\nthat there was a large class of events, the conditions of production\nof which could be said to consist of (1) a comparatively\nfew nearly unchangeable elements, and (2) a vast number\nof independent and very changeable elements. At least if\nthere were any other elements besides these, we are assumed\neither to make special allowance for them, or to omit them\nfrom our enquiry. Now in certain cases, such as games of\nchance, the unchangeable elements may without practical\nerror be regarded as really unchangeable throughout any\nrange of time and space. Hence, as a result, the deductive\nmethod of treatment becomes in their case at once the most\nsimple, natural, and conclusive; but, as a further consequence,\nthe statistics of the events, if we choose to appeal to them,\nmay be collected _ad libitum_ with better and better approximation\nto truth. On the other hand, in all social\napplications of Probability, the unchangeable causes can only\nbe regarded as really unchangeable under many qualifications.\nWe know little or nothing of them directly; they are\noften in reality numerous, indeterminate, and fluctuating;\nand it is only under the guarantee of stringent restrictions of\ntime and place, that we can with any safety attribute to\nthem sufficient fixity to justify our theory. Hence, as a\nresult, the deductive method, under whatever name it may\ngo, becomes totally inapplicable both in theory and practice;\nand, as a further consequence, the appeal to statistics has to\nbe made with the caution in mind that we shall do mischief\nrather than good if we go on collecting too many of them.\n\n19. The results of the last two chapters may be\nsummed up as follows:--We have extended the conception\nof a series obtained in the first chapter; for we have found\nthat these series are mostly presented to us in groups.\nThese groups are found upon examination to be formed upon\napproximately the same type throughout a very wide and\nvaried range of experience; the causes of this agreement we\ndiscussed and explained in some detail. When, however, we\nextend our examination by supposing the series to run to a\nvery great length, we find that they may be divided into two\nclasses separated by important distinctions. In one of these\nclasses (that containing the results of games of chance) the\nconditions of production, and consequently the laws of statistical\noccurrence, may be practically regarded as absolutely\nfixed; and the extent of the divergences from the mean\nseem to know no finite limit. In the other class, on the\ncontrary (containing the bulk of ordinary statistical enquiries),\nthe conditions of production vary with more or less rapidity,\nand so in consequence do the results. Moreover it is often\nimpossible that variations from the mean should exceed a\ncertain amount. The former we may term _ideal_ series. It\nis they alone which show the requisite characteristics with\nany close approach to accuracy, and to make the theory of\nthe subject tenable, we have really to substitute one of this\nkind for one of the less perfect ones of the other class, when\nthese latter are under treatment. The former class have,\nhowever, been too exclusively considered by writers on the\nsubject; and conceptions appropriate only to them, and not\nalways even to them, have been imported into the other\nclass. It is in this way that a general tendency to an excessive\ndeductive or _\u00e0 priori_ treatment of the science has\nbeen encouraged.\n\n\n1. This latter enquiry belongs to what may be termed the more purely\n  logical part of this volume, and is entered on in the course of\n  Chapter VI.\n\n2. For the use of those not acquainted with the common notation\n  employed in this subject, it may be remarked that HH is simply an\n  abbreviated way of saying that the two successive throws of the\n  penny give head; HT that the first of them gives head, and the\n  second tail; and so on with the remaining symbols.\n\n3. I am endeavouring to treat this rule of Sufficient Reason in a way\n  that shall be legitimate in the opinion of those who accept it, but\n  there seem very great doubts whether a contradiction is not involved\n  when we attempt to extract results from it. If the sides are\n  absolutely alike, how can there he any difference between the terms\n  of the series? The succession seems then reduced to a dull\n  uniformity, a mere iteration of the same thing many times; the\n  series we contemplated has disappeared. If the sides are not\n  absolutely alike, what becomes of the applicability of the rule?\n\n4. _Formal Logic_, p. 185. _Principles of Science_, p. 208.\n\n5. The close connection between these subjects is well indicated in\n  the title of Mr Whitworth's treatise, _Choice and Chance_.\n\n6. _Essai Philosophique_. Ed. 1825, p. 74.\n\n7. An opinion prevailed rather at one time (quoted and supported by\n  Quetelet amongst others) that the relative ages of the parents had\n  something to do with the sex of the offspring. If this were so, it\n  would quite bear out the above remarks. As a matter of fact, it\n  should be observed, that the proportion of 106 to 100 does not seem\n  by any means universal in all countries or at all times. For various\n  statistical tables on the subject see Quetelet, _Physique Sociale_,\n  Vol. I. 166, 173, 238.\n\n\n\n\nCHAPTER V.\n\n\n_THE CONCEPTION _RANDOMNESS_ AND ITS SCIENTIFIC TREATMENT._\n\n1. There is a term of frequent occurrence in treatises\non Probability, and which we have already had repeated occasion\nto employ, viz. the designation _random_ applied to an\nevent, as in the expression 'a random distribution'. The\nscientific conception involved in the correct use of this term\nis, I apprehend, nothing more than that of aggregate order\nand individual irregularity (or apparent irregularity), which\nhas been already described in the preceding chapters. A\nbrief discussion of the requisites in this scientific conception,\nand in particular of the nature and some of the reasons for\nthe departure from the popular conception, may serve to\nclear up some of the principal remaining difficulties which\nattend this part of our subject.\n\nThe original,[1] and still popular, signification of the term\nis of course widely different from the scientific. What it\nlooks to is the origin, not the results, of the random performance,\nand it has reference rather to the single action\nthan to a group or series of actions. Thus, when a man\ndraws a bow 'at a venture', or 'at random', we mean only\nto point out the aimless character of the performance;\nwe are contrasting it with the definite intention to hit a\ncertain mark. But it is none the less true, as already\npointed out, that we can only apply processes of inference to\nsuch performances as these when we regard them as being\ncapable of frequent, or rather of indefinitely extended repetition.\n\nBegin with an illustration. Perhaps the best typical\nexample that we can give of the scientific meaning of\nrandom distribution is afforded by the arrangement of the\ndrops of rain in a shower. No one can give a guess whereabouts\nat any instant a drop will fall, but we know that if\nwe put out a sheet of paper it will gradually become uniformly\nspotted over; and that if we were to mark out any\ntwo equal areas on the paper these would gradually tend\nto be struck equally often.\n\n2. I. Any attempt to draw inferences from the assumption\nof random arrangement must postulate the occurrence\nof this particular state of things at some stage or\nother. But there is often considerable difficulty, leading occasionally\nto some arbitrariness, in deciding the particular\nstage at which it ought to be introduced.\n\n(1) Thus, in many of the problems discussed by mathematicians,\nwe look as entirely to the results obtained, and\nthink as little of the actual process by which they are obtained,\nas when we are regarding the arrangement of the drops of\nrain. A simple example of this kind would be the following.\nA pawn, diameter of base one inch, is placed at random on\na chess-board, the diameter of the squares of which is one inch\nand a quarter: find the chance that its base shall lie across\none of the intersecting lines. Here we may imagine the\npawns to be so to say rained down vertically upon the board,\nand the question is to find the ultimate proportion of those\nwhich meet a boundary line to the total of those which fall.\nThe problem therefore becomes a merely geometrical one,\nviz. to determine the ratio of a certain area on the board to\nthe whole area. The determination of this ratio is all that\nthe mathematician ever takes into account.\n\nNow take the following. A straight brittle rod is broken\nat random in two places: find the chance that the pieces can\nmake a triangle.[2] Since the only condition for making a\ntriangle with three straight lines is that each two shall be\ngreater than the third, the problem seems to involve the\nsame general conception as in the former case. We must\nconceive such rods breaking at one pair of spots after\nanother,--no one can tell precisely where,--but showing the\nsame ultimate tendency to distribute these spots throughout\nthe whole length uniformly. As in the last case, the mathematician\nthinks of nothing but this final result, and pays no\nheed to the process by which it may be brought about. Accordingly\nthe problem is again reduced to one of mensuration,\nthough of a somewhat more complicated character.\n\n3. (2) In another class of cases we have to contemplate\nan intermediate process rather than a final result; but the\nsame conception has to be introduced here, though it is now\napplied to the former stage, and in consequence will not in\ngeneral apply to the latter.\n\nFor instance: a shot is fired at random from a gun whose\nmaximum range (i.e. at 45\u00b0 elevation) is 3000 yards: what is\nthe chance that the actual range shall exceed 2000 yards?\nThe ultimately uniform (or random) distribution here is\ncommonly assumed to apply to the various directions in\nwhich the gun can be pointed; all possible directions above\nthe horizontal being equally represented in the long run.\nWe have therefore to contemplate a surface of uniform distribution,\nbut it will be the surface, not of the ground, but\nof a hemisphere whose centre is occupied by the man who\nfires. The ultimate distribution of the bullets on the spots\nwhere they strike the ground will not be uniform. The\nproblem is in fact to discover the law of variation of the\ndensity of distribution.\n\nThe above is, I presume, the treatment generally adopted\nin solving such a problem. But there seems no absolute\nnecessity for any such particular choice. It is surely open to\nany one to maintain[3] that his conception of the randomness of\nthe firing is assigned by saying that it is likely that a man\nshould begin by facing towards any point of the compass indifferently,\nand then proceed to raise his gun to any angle\nindifferently. The stage of ultimately uniform distribution\nhere has receded a step further back. It is not assigned\ndirectly to the surface of an imaginary hemisphere, but to\nthe lines of altitude and azimuth drawn on that surface.\nAccordingly, the distribution over the hemisphere itself will\nnot now be uniform,--there will be a comparative crowding\nup towards the pole,--and the ultimate distribution over the\nground will not be the same as before.\n\n4. Difficulties of this kind, arising out of the uncertainty\nas to what stage should be selected for that of uniform\ndistribution, will occasionally present themselves. For\ninstance: let a book be taken at random out of a bookcase;\nwhat is the chance of hitting upon some assigned volume?\nI hardly know how this question would commonly be treated.\nIf we were to set our man opposite the middle of the shelf\nand inquire what would generally happen in practice, supposing\nhim blindfolded, there cannot be much doubt that\nthe volumes would not be selected equally often. On the\ncontrary, it is likely that there would be a tendency to increased\nfrequency about a centre indicated by the height\nof his shoulder, and (unless he be left-handed) a trifle to the\nright of the point exactly opposite his starting point.\n\nIf the question were one which it were really worth\nwhile to work out on these lines we should be led a long\nway back. Just as we imagined our rifleman's position (on\nthe second supposition) to be determined by two independent\ncoordinates of assumed continuous and equal facility,\nso we might conceive our making the attempt to analyse the\nman's movements into a certain number of independent\nconstituents. We might suppose all the various directions\nfrom his starting point, along the ground, to be equally\nlikely; and that when he reaches the shelves the random\nmotion of his hand is to be regulated after the fashion of a\nshot discharged at random.\n\nThe above would be one way of setting about the statement\nof the problem. But the reader will understand that\nall which I am here proposing to maintain is that in these,\nas in every similar case, we always encounter, under this\nconception of 'randomness', at some stage or other, this\npostulate of ultimate uniformity of distribution over some\nassigned magnitude: either time; or space, linear, superficial,\nor solid. But the selection of the stage at which this is to\nbe applied may give rise to considerable difficulty, and even\narbitrariness of choice.\n\n5. Some years ago there was a very interesting discussion\nupon this subject carried on in the mathematical part of\nthe _Educational Times_ (see, especially, Vol. VII.). As not\nunfrequently happens in mathematics there was an almost\nentire accord amongst the various writers as to the assumptions\npractically to be made in any particular case, and therefore\nas to the conclusion to be drawn, combined with a very\nconsiderable amount of difference as to the axioms and definitions\nto be employed. Thus Mr M. W. Crofton, with the\nsubstantial agreement of Mr Woolhouse, laid it down unhesitatingly\nthat \"at random\" has \"a very clear and definite\nmeaning; one which cannot be better conveyed than by Mr\nWilson's definition, '_according to no law_'; and in this sense\nalone I mean to use it.\" According to any scientific interpretation\nof 'law' I should have said that where there was\nno law there could be no inference. But ultimate tendency\ntowards equality of distribution is as much taken for granted\nby Mr Crofton as by any one else: in fact he makes this a\ndeduction from his definition:--\"As this infinite system of\nparallels are drawn according to no law, they are as thickly\ndisposed along any part of the [common] perpendicular as\nalong any other\" (VII. p. 85). Mr Crofton holds that any\nkind of _unequal_ distribution would imply law,--\"If the points\n[on a plane] tended to become denser in any part of the plane\nthan in another, there must be some law attracting them\nthere\" (ib. p. 84). The same view is enforced in his paper\non _Local Probability_ (in the _Phil. Trans._, Vol. 158). Surely\nif they tend to become _equally_ dense this is just as much\na case of regularity or law.\n\nIt may be remarked that wherever any serious practical\nconsequences turn upon duly securing the desired randomness,\nit is always so contrived that no design or awkwardness\nor unconscious one-sidedness shall disturb the result. The\nprincipal case in point here is of course afforded by games of\nchance. What we want, when we toss a die, is to secure that\nall numbers from 1 to 6 shall be equally often represented in\nthe long run, but that no person shall be able to predict the\nindividual occurrence. We might, in our statement of a\nproblem, as easily postulate 'a number _thought of_ at random'\nas 'a shot fired at random', but no one would risk his chances\nof gain and loss on the supposition that this would be done\nwith continued fairness. Accordingly, we construct a die\nwhose sides are accurately alike, and it is found that we may\ndo almost what we like with this, at any previous stage to\nthat of its issue from the dice box on to the table, without\ninterfering with the random nature of the result.\n\n6. II. Another characteristic in which the scientific\nconception seems to me to depart from the popular or original\nsignification is the following. The area of distribution which\nwe take into account must be a finite or limited one. The\nnecessity for this restriction may not be obvious at first sight,\nbut the consideration of one or two examples will serve to\nindicate the point at which it makes itself felt. Suppose\nthat one were asked to choose a number at random, not\nfrom a finite range, but from the inexhaustible possibilities\nof enumeration. In the popular sense of the term,--i.e. of\nuttering a number without pausing to choose,--there is no\ndifficulty. But a moment's consideration will show that no\narrangement even tending towards ultimately uniform distribution\ncan be secured in this way. No _average_ could be\nstruck with ever increasing steadiness. So with spatial\ninfinity. We can rationally speak of choosing a point at\nrandom in a given straight line, area, or volume. But if we\nsuppose the line to have no end, or the selection to be made\nin infinite space, the basis of ultimate tendency towards\nwhat may be called the equally thick deposit of our random\npoints fails us utterly.\n\nSimilarly in any other example in which one of the\nmagnitudes is unlimited. Suppose I fling a stick at random\nin a horizontal plane against a row of iron railings and\ninquire for the chance of its passing through without touching\nthem. The problem bears some analogy to that of the\nchessmen, and so far as the motion of translation of the\nstick is concerned (if we begin with this) it presents no\ndifficulty. But as regards the rotation it is otherwise. For\nany assigned linear velocity there is a certain angular velocity\n_below_ which the stick may pass through without contact,\nbut _above_ which it cannot. And inasmuch as the former\nrange is limited and the latter is unlimited, we encounter\nthe same impossibility as before in endeavouring to conceive\na uniform distribution. Of course we might evade this\nparticular difficulty by beginning with an estimate of the\nangular velocity, when we should have to repeat what has\njust been said, mutatis mutandis, in reference to the linear\nvelocity.\n\n7. I am of course aware that there are a variety of\nproblems current which seem to conflict with what has just\nbeen said, but they will all submit to explanation. For instance;\nWhat is the chance that three straight lines, taken\nor drawn at random, shall be of such lengths as will admit of\ntheir forming a triangle? There are two ways in which we\nmay regard the problem. We may, for one thing, start with\nthe assumption of three lines not greater than a certain\nlength n, and then determine towards what limit the chance\ntends as n increases unceasingly. Or, we may maintain that\nthe question is merely one of _relative proportion_ of the three\nlines. We may then start with any magnitude we please to\nrepresent one of the lines (for simplicity, say, the longest of\nthem), and consider that all possible shapes of a triangle\nwill be represented by varying the lengths of the other two.\nIn either case we get a definite result without need to make\nan attempt to conceive any random selection from the infinity\nof possible length.\n\nSo in what is called the \"three-point problem\":--Three\npoints in space are selected at random; find the chance of\ntheir forming an acute-angled triangle. What is done is to\nstart with a closed volume,--say a sphere, from its superior\nsimplicity,--find the chance (on the assumption of uniform\ndistribution within this volume); and then conceive the continual\nenlargement without limit of this sphere. So regarded\nthe problem is perfectly consistent and intelligible, though I\nfail to see why it should be termed a random selection _in\nspace_ rather than in a sphere. Of course if we started with\na different volume, say a cube, we should get a different\nresult; and it is therefore contended (e.g. by Mr Crofton in\nthe _Educational Times_, as already referred to) that infinite\nspace is more naturally and appropriately regarded as tended\ntowards by the enlargement of a sphere than by that of a\ncube or any other figure.\n\nAgain: A group of integers is taken at random; show\nthat the number thus taken is more likely to be odd than\neven. What we do in answering this is to start with any\nfinite number n, and show that of all the possible combinations\nwhich can be made within this range there are\nmore odd than even. Since this is true irrespective of the\nmagnitude of n, we are apt to speak as if we could conceive\nthe selection being made at random from the true infinity\ncontemplated in numeration.\n\n8. Where these conditions cannot be secured then it\nseems to me that the attempt to assign any finite value to\nthe probability fails. For instance, in the following problem,\nproposed by Mr J. M. Wilson, \"Three straight lines are\ndrawn at random on an infinite plane, and a fourth line is\ndrawn at random to intersect them: find the probability of\nits passing through the triangle formed by the other three\"\n(_Ed. Times_, Reprint, Vol. V. p. 82), he offers the following\nsolution: \"Of the four lines, two must and two must not pass\nwithin the triangle formed by the remaining three. Since\nall are drawn at random, the chance that the last drawn\nshould pass through the triangle formed by the other three\nis consequently 1/2.\"\n\nI quote this solution because it seems to me to illustrate\nthe difficulty to which I want to call attention. As the\nproblem is worded, a triangle is supposed to be assigned by\nthree straight lines. However large it may be, its size bears\nno finite ratio whatever to the indefinitely larger area outside\nit; and, so far as I can put any intelligible construction\non the supposition, the chance of drawing a fourth random\nline which should happen to intersect this finite area must\nbe reckoned as zero. The problem Mr Wilson has solved\nseems to me to be a quite different one, viz. \"Given four\nintersecting straight lines, find the chance that we should,\nat random, select one that passes through the triangle formed\nby the other three.\"\n\nThe same difficulty seems to me to turn up in most other\nattempts to apply this conception of randomness to real\ninfinity. The following seems an exact analogue of the\nabove problem:--A number is selected at random, find the\nchance that another number selected at random shall be\ngreater than the former;--the answer surely must be that\nthe chance is unity, viz. certainty, because the range above\nany assigned number is infinitely greater than that below it.\nOr, expressed in the only language in which I can understand\nthe term 'infinity', what I mean is this. If the first\nnumber be m and I am restricted to selecting up to n\n(n > m) then the chance of exceeding m is n - m : n; if I\nam restricted to 2n then it is 2n - m : 2n and so on. That\nis, however large n and m may be the expression is always\nintelligible; but, _m being chosen first_, n may be made as\nmuch larger than m as we please: i.e. the chance may be\nmade to approach as near to unity as we please.\n\nI cannot but think that there is a similar fallacy in De Morgan's\nadmirably suggestive paper on _Infinity_ (_Camb.\nPhil. Trans._ Vol. 11.) when he is discussing the \"three-point\nproblem\":--i.e. given three points taken at random find the\nchance that they shall form an acute-angled triangle. All\nthat he shows is, that if we start with _one side as given_ and\nconsider the subsequent possible positions of the opposite\nvertex, there are infinitely as many such positions which\nwould form an acute-angled triangle as an obtuse: but, as\nbefore, this is solving a different problem.\n\n9. The nearest approach I can make towards true indefinite\nrandomness, or random selection from true indefiniteness,\nis as follows. Suppose a circle with a tangent line extended\nindefinitely in each direction. Now from the centre draw\nradii at random; in other words, let the semicircumference\nwhich lies towards the tangent be ultimately uniformly intersected\nby the radii. Let these radii be then produced so as\nto intersect the tangent line, and consider the distribution\nof these points of intersection. We shall obtain in the result\n_one_ characteristic of our random distribution; i.e. no portion\nof this tangent, however small or however remote, but will\nfind itself in the position ultimately of any small portion of\nthe pavement in our supposed continual rainfall. That is,\nany such elementary patch will become more and more closely\ndotted over with the points of intersection. But the other\nessential characteristic, viz. that of ultimately _uniform_ distribution,\nwill be missing. There will be a special form of\ndistribution,--what in fact will have to be discussed in a\nfuture chapter under the designation of a 'law of error',--by\nvirtue of which the concentration will tend to be greatest at\na certain point (that of contact with the circle), and will thin\nout from here in each direction according to an easily\ncalculated formula. The existence of such a state of things\nas this is quite opposed to the conception of true randomness.\n\n10. III. Apart from definitions and what comes of\nthem, perhaps the most important question connected with\nthe conception of Randomness is this: How in any given\ncase are we to determine whether an observed arrangement\nis to be considered a random one or not? This question will\nhave to be more fully discussed in a future chapter, but we\nare already in a position to see our way through some of the\ndifficulties involved in it.\n\n(1) If the events or objects under consideration are supposed\nto be continued indefinitely, or if we know enough\nabout the mode in which they are brought about to detect\ntheir ultimate tendency,--or even, short of this, if they are\nnumerous enough to be beyond practical counting,--there is\nno great difficulty. We are simply confronted with a question\nof fact, to be settled like other questions of fact. In the\ncase of the rain-drops, watch two equal squares of pavement\nor other surfaces, and note whether they come to be more\nand more densely uniformly and evenly spotted over: if they\ndo, then the arrangement is what we call a random one. If\nI want to know whether a tobacco-pipe really breaks at random,\nand would therefore serve as an illustration of the\nproblem proposed some pages back, I have only to drop\nenough of them and see whether pieces of all possible lengths\nare equally represented in the long run. Or, I may argue\ndeductively, from what I know about the strength of materials\nand the molecular constitution of such bodies, as to\nwhether fractures of small and large pieces are all equally\nlikely to occur.\n\n11. The reader's attention must be carefully directed\nto a source of confusion here, arising out of a certain cross-division.\nWhat we are now discussing is a question of fact,\nviz. the nature of a certain ultimate arrangement; we are\nnot discussing the particular way in which it is brought\nabout. In other words, the antithesis is between what is and\nwhat is not random: it is not between what is random and\nwhat is designed. As we shall see in a few moments it is\nquite possible that an arrangement which is the result,--if\never anything were so,--of 'design', may nevertheless present\nthe unmistakeable stamp of randomness of arrangement.\n\nConsider a case which has been a good deal discussed,\nand to which we shall revert again: the arrangement of the\nstars. The question here is rather complicated by the fact\nthat we know nothing about the actual mutual positions of\nthe stars, all that we can take cognizance of being their apparent\nor visible places as projected upon the surface of a\nsupposed sphere. Appealing to what alone we can thus\nobserve, it is obvious that the arrangement, as a whole, is\nnot of the random sort. The Milky Way and the other resolvable\nnebul\u00e6, as they present themselves to us, are as obvious\nan infraction of such an arrangement as would be the\noccurrence here and there of patches of ground in a rainfall\nwhich received a vast number more drops than the spaces\nsurrounding them. If we leave these exceptional areas out\nof the question and consider only the stars which are visible\nby the naked eye or by slight telescopic power, it seems\nequally certain that the arrangement _is_, for the most part, a\nfairly representative random one. By this we mean nothing\nmore than the fact that when we mark off any number of\nequal areas on the visible sphere these are found to contain\napproximately the same number of stars.\n\nThe actual arrangement of the stars in space _may_ also\nbe of the same character: that is, the apparently denser\naggregation may be apparent only, arising from the fact that\nwe are looking through regions which are not more thickly\noccupied but are merely more extensive. The alternative\nbefore us, in fact, is this. If the whole volume, so to say, of\nthe starry heavens is tolerably regular in shape, then the\narrangement of the stars is not of the random order; if that\nvolume is very irregular in shape, it is possible that the arrangement\nwithin it may be throughout of that order.\n\n12. (2) When the arrangement in question includes\nbut a comparatively small number of events or objects, it\nbecomes much more difficult to determine whether or not it\nis to be designated a random one. In fact we have to shift\nour ground, and to decide not by what has been actually\nobserved but by what we have reason to conclude would be\nobserved if we could continue our observation much longer.\nThis introduces what is called 'Inverse Probability', viz. the\ndetermination of the nature of a cause from the nature of the\nobserved effect; a question which will be fully discussed in\na future chapter. But some introductory remarks may be\nconveniently made here.\n\nEvery problem of Probability, as the subject is here understood,\nintroduces the conception of an ultimate limit, and\ntherefore presupposes an indefinite possibility of repetition.\nWhen we have only a finite number of occurrences before us,\n_direct_ evidence of the character of their arrangement fails us,\nand we have to fall back upon the nature of the agency\nwhich produces them. And as the number becomes smaller\nthe confidence with which we can estimate the nature of the\nagency becomes gradually less.\n\nBegin with an intermediate case. There is a small lawn,\nsprinkled over with daisies: is this a random arrangement?\nWe feel some confidence that it is so, on mere inspection;\nmeaning by this that (negatively) no trace of any regular\npattern can be discerned and (affirmatively) that if we take\nany moderately small area, say a square yard, we shall find\nmuch about the same number of the plants included in it.\nBut we can help ourselves by an appeal to the known agency\nof distribution here. We know that the daisy spreads by\nseed, and considering the effect of the wind and the continued\nsweeping and mowing of the lawn we can detect causes at\nwork which are analogous to those by which the dealing of\ncards and the tossing of dice are regulated.\n\nIn the above case the appeal to the process of production\nwas subsidiary, but when we come to consider the nature of\na very small succession or group this appeal becomes much\nmore important. Let us be told of a certain succession of\n'heads' and 'tails' to the number of ten. The range here is\nfar too small for decision, and unless we are told whether the\nagent who obtained them was tossing or designing we are\nquite unable to say whether or not the designation of 'random'\nought to be applied to the result obtained. The truth\nmust never be forgotten that though 'design' is sure to\nbreak down in the long run if it make the attempt to produce\ndirectly the semblance of randomness,[4] yet for a short\nspell it can simulate it perfectly. Any short succession, say\nof heads and tails, may have been equally well brought\nabout by tossing or by deliberate choice.\n\n13. The reader will observe that this question of\nrandomness is being here treated as simply one of ultimate\nstatistical fact. I have fully admitted that this is not the\nprimitive conception, nor is it the popular interpretation,\nbut to adopt it seems the only course open to us if we are to\ndraw inferences such as those contemplated in Probability.\nWhen we look to the producing agency of the ultimate\narrangement we may find this very various. It may prove\nitself to be (a few stages back) one of conscious deliberate\npurpose, as in drawing a card or tossing a die: it may be\nthe outcome of an extremely complicated interaction of many\nnatural causes, as in the arrangement of the flowers scattered\nover a lawn or meadow: it may be of a kind of which we\nknow literally nothing whatever, as in the case of the actual\narrangement of the stars relatively to each other.\n\nThis was the state of things had in view when it was\nsaid a few pages back that randomness and design would\nresult in something of a cross-division. Plenty of arrangements\nin which design had a hand, a stage or two back, can\nbe mentioned, which would be quite indistinguishable in\ntheir results from those in which no design whatever could\nbe traced. Perhaps the most striking case in point here is\nto be found in the arrangement of the digits in one of the\nnatural arithmetical constants, such as \u03c0 or e, or in a table\nof logarithms. If we look to the process of production of\nthese digits, no extremer instance can be found of what we\nmean by the antithesis of randomness: every figure has its\nnecessarily pre-ordained position, and a moment's flagging of\nintention would defeat the whole purpose of the calculator.\nAnd yet, if we look to results only, no better instance can\nbe found than one of these rows of digits if it were intended\nto illustrate what we practically understand by a chance\narrangement of a number of objects. Each digit occurs\napproximately equally often, and this tendency develops as\nwe advance further: the mutual juxtaposition of the digits\nalso shows the same tendency, that is, any digit (say 5) is\njust as often followed by 6 or 7 as by any of the others. In\nfact, if we were to take the whole row of hitherto calculated\nfigures, cut off the first five as familiar to us all, and contemplate\nthe rest, no one would have the slightest reason\nto suppose that these had not come out as the results of a\ndie with ten equal faces.\n\n14. If it be asked _why_ this is so, a rather puzzling\nquestion is raised. Wherever physical causation is involved\nwe are generally understood to have satisfied the demand\nimplied in this question if we assign antecedents which will\nbe followed regularly by the event before us; but in geometry\nand arithmetic there is no opening for antecedents. What\nwe then commonly look for is a demonstration, i.e. the resolution\nof the observed fact into axioms if possible, or at\nany rate into admitted truths of wider generality. I do not\nknow that a demonstration can be given as to the existence\nof this characteristic of statistical randomness in such successions\nof digits as those under consideration. But the\nfollowing remarks may serve to shift the onus of unlikelihood\nby suggesting that the preponderance of analogy is\nrather in favour of the existence.\n\nTake the well-known constant \u03c0 for consideration. This\nstands for a quantity which presents itself in a vast number\nof arithmetical and geometrical relations; let us take for\nexamination the best known of these, by regarding it as\nstanding for the ratio of the circumference to the diameter\nof a circle. So regarded, it is nothing more than a simple\ncase of the measurement of a magnitude by an arbitrarily\nselected unit. Conceive then that we had before us a rod\nor line and that we wished to measure it with absolute\naccuracy. We must suppose--if we are to have a suitable\nanalogue to the determination of \u03c0 to several hundred\nfigures,--that by the application of continued higher magnifying\npower we can detect ever finer subdivisions in the\ngraduation. We lay our rod against the scale and find it,\nsay, fall between 31 and 32 inches; we then look at the\nnext division of the scale, viz. that into tenths of an inch.\nCan we see the slightest reason why the number of these\ntenths should be other than independent of the number of\nwhole inches? The \"piece over\" which we are measuring\nmay in fact be regarded as an entirely new piece, which had\nfallen into our hands after that of 31 inches had been\nmeasured and done with; and similarly with every successive\npiece over, as we proceed to the ever finer and finer divisions.\n\nSimilar remarks may be made about most other incommensurable\nquantities, such as irreducible roots. Conceive\ntwo straight lines at right angles, and that we lay off a\ncertain number of inches along each of these from the point\nof intersection; say two and five inches, and join the extremities\nof these so as to form the diagonal of a right-angled\ntriangle. If we proceed to measure this diagonal in terms\nof either of the other lines we are to all intents and purposes\nextracting a square root. We should expect, rather than\notherwise, to find here, as in the case of \u03c0, that incommensurability\nand resultant randomness of order in the digits\nwas the rule, and commensurability was the exception. Now\nand then, as when the two sides were three and four, we\nshould find the diagonal commensurable with them; but\nthese would be the occasional exceptions, or rather they\nwould be the comparatively finite exceptions amidst the\nindefinitely numerous cases which furnished the rule.\n\n15. The best way perhaps of illustrating the truly\nrandom character of such a row of figures is by appealing to\ngraphical aid. It is not easy here, any more than in ordinary\nstatistics, to grasp the import of mere figures; whereas the\narrangement of groups of points or lines is much more\nreadily seized. The eye is very quick in detecting any\nsymptoms of regularity in the arrangement, or any tendency\nto denser aggregation in one direction than in another.\nHow then are we to dispose our figures so as to force them\nto display their true character? I should suggest that we\nset about _drawing a line at random_; and, since we cannot\ntrust our own unaided efforts to do this, that we rely upon\nthe help of such a table of figures to do it for us, and then\nexamine with what sort of efficiency they can perform the\ntask. The problem of drawing _straight_ lines at random,\nunder various limitations of direction or intersection, is\nfamiliar enough, but I do not know that any one has suggested\nthe drawing of a line whose shape as well as position\nshall be of a purely random character. For simplicity we\nsuppose the line to be confined to a plane.\n\nThe definition of such a line does not seem to involve\nany particular difficulty. Phrased in accordance with the\nordinary language we should describe it as the path (i.e. any\npath) traced out by a point which at every moment is as\nlikely to move in any one direction as in any other. That\nwe could not ourselves draw such a line, and that we could\nnot get it traced by any physical agency, is certain. The\nmere inertia of any moving body will always give it a\ntendency, however slight, to go on in a straight line at each\nmoment, instead of being instantly responsive to instantaneously\nvarying dictates as to its direction of motion. Nor can\nwe conceive or picture such a line in its ultimate or ideal condition.\nBut it is easy to give a graphical approximation to it,\nand it is easy also to show how this approximation may be\ncarried on as far as we please towards the ideal in question.\n\nWe may proceed as follows. Take a sheet of the ordinary\nruled paper prepared for the graphical exposition of curves.\nSelect as our starting point the intersection of two of these\nlines, and consider the eight 'points of the compass' indicated\nby these lines and the bisections of the contained\nright angles.[5] For suggesting the random selection amongst\nthese directions let them be numbered from 0 to 7, and\nlet us say that a line measured due 'north' shall be designated\nby the figure 0, 'north-east' by 1, and so on. The\nselection amongst these numbers, and therefore directions, at\nevery corner, might be handed over to a die with eight faces;\nbut for the purpose of the illustration in view we select the\ndigits 0 to 7 as they present themselves in the calculated\nvalue of \u03c0. The sort of path along which we should\ntravel by a series of such steps thus taken at random\nmay be readily conceived; it is given at the end of this\nchapter.\n\nFor the purpose with which this illustration was proposed,\nviz. the graphical display of the succession of digits\nin any one of the incommensurable constants of arithmetic\nor geometry, the above may suffice. After actually testing\nsome of them in this way they seem to me, so far as the eye,\nor the theoretical principles to be presently mentioned, are\nany guide, to answer quite fairly to the description of randomness.\n\n16. As we are on the subject, however, it seems worth\ngoing farther by enquiring how near we could get to the\nideal of randomness of direction. To carry this out completely\ntwo improvements must be made. For one thing,\ninstead of confining ourselves to eight directions we must\nadmit an infinite number. This would offer no great difficulty;\nfor instead of employing a small number of digits we\nshould merely have to use some kind of circular teetotum\nwhich would rest indifferently in any direction. But in the\nnext place instead of short finite steps we must suppose them\nindefinitely short. It is here that the actual unattainability\nmakes itself felt. We are familiar enough with the device,\nemployed by Newton, of passing from the discontinuous\npolygon to the continuous curve. But we can resort to this\ndevice because the ideal, viz. the curve, is as easily drawn\n(and, I should say, as easily conceived or pictured) as any of\nthe steps which lead us towards it. But in the case before\nus it is otherwise. The line in question will remain discontinuous,\nor rather angular, to the last: for its angles do\nnot tend even to lose their sharpness, though the fragments\nwhich compose them increase in number and diminish in\nmagnitude without any limit. And such an ideal is not conceivable\nas an ideal. It is as if we had a rough body under\nthe microscope, and found that as we subjected it to higher\nand higher powers there was no tendency for the angles to\nround themselves off. Our 'random line' must remain as\n'spiky' as ever, though the size of its spikes of course\ndiminishes without any limit.\n\nThe case therefore seems to be this. It is easy, in words,\nto indicate the conception by speaking of a line which at\nevery instant is as likely to take one direction as another.\nIt is easy moreover to draw such a line with any degree\nof minuteness which we choose to demand. But it is not\npossible to conceive or picture the line in its ultimate form.[6]\nThere is in fact no 'limit' here, intelligible to the understanding\nor picturable by the imagination (corresponding to\nthe asymptote of a curve, or the continuous curve to the\nincessantly developing polygon), towards which we find ourselves\ncontinually approaching, and which therefore we are\napt to conceive ourselves as ultimately attaining. The usual\nassumption therefore which underlies the Newtonian infinitesimal\ngeometry and the Differential Calculus, ceases to\napply here.\n\n17. If we like to consider such a line in one of its\napproximate stages, as above indicated, it seems to me that\nsome of the usual theorems of Probability, where large\nnumbers are concerned, may safely be applied. If it be\nasked, for instance, whether such a line will ultimately tend\nto stray indefinitely far from its starting point, Bernoulli's\n'Law of Large Numbers' may be appealed to, in virtue of\nwhich we should say that it was excessively unlikely that its\ndivergence should be relatively great. Recur to our graphical\nillustration, and consider first the resultant deviation\nof the point (after a great many steps) right or left of the\nvertical line through the starting point. Of the eight admissible\nmotions at each stage two will not affect this relative\nposition, whilst the other six are equally likely to move us a\nstep to the right or to the left. Our resultant 'drift' therefore\nto the right or left will be analogous to the resultant\ndifference between the number of heads and tails after a\ngreat many tosses of a penny. Now the well-known outcome\nof such a number of tosses is that ultimately the\n_proportional_ approximation to the _\u00e0 priori_ probability, i.e. to\nequality of heads and tails, is more and more nearly carried\nout, but that the _absolute_ deflection is more and more widely\ndisplayed.\n\nApplying this to the case in point, and remembering\nthat the results apply equally to the horizontal and vertical\ndirections, we should say that after any very great number\nof such 'steps' as those contemplated, the ratio of our distance\nfrom the starting point to the whole distance travelled\nwill pretty certainly be small, whereas the actual distance\nfrom it would be large. We should also say that the longer\nwe continued to produce such a line the more pronounced\nwould these tendencies become. So far as concerns this test,\nand that afforded by the general appearance of the lines\ndrawn,--this last, as above remarked, being tolerably trustworthy,--I\nfeel no doubt as to the generally 'random'\ncharacter of the rows of figures displayed by the incommensurable\nor irrational ratios in question.\n\nAs it may interest the reader to see an actual specimen\nof such a path I append one representing the arrangement\nof the eight digits from 0 to 7 in the value of \u03c0. The data\nare taken from Mr Shanks' astonishing performance in the\ncalculation of this constant to 707 places of figures (_Proc. of\nR. S._, XXI. p. 319). Of these, after omitting 8 and 9, there\nremain 568; the diagram represents the course traced out\nby following the direction of these as the clue to our path.\nMany of the steps have of course been taken in opposite\ndirections twice or oftener. The result seems to me to\nfurnish a very fair graphical indication of randomness. I\nhave compared it with corresponding paths furnished by\nrows of figures taken from logarithmic tables, and in other\nways, and find the results to be much the same.\n\n[Figure: Digits of \u03c0 as a path.]\n\n1. According to Prof. Skeat (_Etymological Dictionary_) the earliest\n  known meaning is that of _furious_ action, as in a charge of\n  cavalry. The etymology, he considers, is connected with the\n  Teutonic word _rand_ (brim), and implies the furious and irregular\n  action of a river full to the brim.\n\n2. See the problem paper of Jan. 18, 1854, in the Cambridge\n  Mathematical Tripos.\n\n3. As, according to Mr H. Godfray, the majority of the candidates\n  _did_ assume when the problem was once proposed in an\n  examination. See the _Educational Times_ (Reprint, Vol. VII.\n  p. 99.)\n\n4. Vide p. 68.\n\n5. It would of course be more complete to take _ten_ alternatives of\n  direction, and thus to omit none of the digits; but this is much\n  more troublesome in practice than to confine ourselves to eight.\n\n6. Any more than we picture the shape of an equiangular spiral _at the\n  centre_.\n\n\n\n\nCHAPTER VI.[1]\n\n\n_THE SUBJECTIVE SIDE OF PROBABILITY. MEASUREMENT OF BELIEF._\n\n1. Originally written in somewhat of a spirit of protest against what\n  seemed to me the prevalent disposition to follow De Morgan in taking\n  too subjective a view of the science. In reading it through now I\n  cannot find any single sentence to which I could take distinct\n  objection, though I must admit that if I were writing it entirely\n  afresh I should endeavour to express myself with less emphasis, and\n  I have made alterations in that direction. The reader who wishes to\n  see a view not substantially very different from mine, but expressed\n  with a somewhat opposite emphasis, can refer to Mr F. Y. Edgeworth's\n  article on \"The Philosophy of Chance\" (_Mind_, Vol. IX.)\n\n\n1. Having now obtained a clear conception of a\ncertain kind of series, the next enquiry is, What is to be\ndone with this series? How is it to be employed as a means\nof making inferences? The general step that we are now\nabout to take might be described as one from the objective\nto the subjective, from the things themselves to the state of\nour minds in contemplating them.\n\nThe reader should observe that a substitution has, in a\ngreat number of cases, already been made as a first stage\ntowards bringing the things into a shape fit for calculation.\nThis substitution, as described in former chapters, is, in a\nmeasure, a process of _idealization_. The series we actually\nmeet with are apt to show a changeable type, and the individuals\nof them will sometimes transgress their licensed irregularity.\nHence they have to be pruned a little into shape, as\nnatural objects almost always have before they are capable of\nbeing accurately reasoned about. The form in which the\nseries emerges is that of a series with a fixed type. This\nimaginary or ideal series is the basis of our calculation.\n\n2. It must not be supposed that this is at all at variance\nwith the assertion previously made, that Probability is a\nscience of inference about real things; it is only by a substitution\nof the above kind that we are enabled to reason about\nthe things. In nature nearly all phenomena present themselves\nin a form which departs from that rigorously accurate\none which scientific purposes mostly demand, so we have to\nintroduce an imaginary series, which shall be free from any\nsuch defects. The only condition to be fulfilled is, that the\nsubstitution is to be as little arbitrary, that is, to vary from\nthe truth as slightly, as possible. This kind of substitution\ngenerally passes without notice when natural objects of any\nkind are made subjects of exact science. I direct distinct\nattention to it here simply from the apprehension that want\nof familiarity with the subject-matter might lead some readers\nto suppose that it involves, in this case, an exceptional deflection\nfrom accuracy in the formal process of inference.\n\nIt may be remarked also that the adoption of this imaginary\nseries offers no countenance whatever to the doctrine\ncriticised in the last chapter, in accordance with which it was\nsupposed that our series possessed a fixed unchangeable type\nwhich was merely the \"development of the probabilities\" of\nthings, to use Laplace's expression. It differs from anything\ncontemplated on that hypothesis by the fact that it is to be\nrecognized as a necessary substitution of our own for the\nactual series, and to be kept in as close conformity with facts as\npossible. It is a mere fiction or artifice necessarily resorted\nto for the purpose of calculation, and for this purpose only.\n\nThis caution is the more necessary, because in the example\nthat I shall select, and which belongs to the most favourite\nclass of examples in this subject, the substitution becomes\naccidentally unnecessary. The things, as has been repeatedly\npointed out, may sometimes need no trimming, because in\nthe form in which they actually present themselves they _are_\nalmost idealized. In most cases a good deal of alteration is\nnecessary to bring the series into shape, but in some--prominently\nin the case of games of chance--we find the alterations,\nfor all practical purposes, needless.\n\n3. We start then, from such a series as this, upon the\nenquiry, What kind of inference can be made about it? It\nmay assist the logical reader to inform him that our first step\nwill be analogous to one class of what are commonly known\nas _immediate_ inferences,--inferences, that is, of the type,--'All\nmen are mortal, therefore any particular man or men\nare mortal.' This case, simple and obvious as it is in Logic,\nrequires very careful consideration in Probability.\n\nIt is obvious that we must be prepared to form an opinion\nupon the propriety of taking the step involved in making\nsuch an inference. Hitherto we have had as little to do as\npossible with the irregular individuals; we have regarded\nthem simply as fragments of a regular series. But we cannot\nlong continue to neglect all consideration of them. Even if\nthese events in the gross be tolerably certain, it is not only\nin the gross that we have to deal with them; they constantly\ncome before us a few at a time, or even as individuals,\nand we have to form some opinion about them in this\nstate. An insurance office, for instance, deals with numbers\nlarge enough to obviate most of the uncertainty, but\neach of their transactions has another party interested in\nit--What has the man who insures to say to their proceedings?\nfor to him this question becomes an individual one.\nAnd even the office itself receives its cases singly, and would\ntherefore like to have as clear views as possible about these\nsingle cases. Now, the remarks made in the preceding chapters\nabout the subjects which Probability discusses might seem to\npreclude all enquiries of this kind, for was not ignorance of\nthe individual presupposed to such an extent that even (as\nwill be seen hereafter) causation might be denied, within\nconsiderable limits, without affecting our conclusions? The\nanswer to this enquiry will require us to turn now to the\nconsideration of a totally distinct side of the question, and\none which has not yet come before us. Our best introduction\nto it will be by the discussion of a special example.\n\n4. Let a penny be tossed up a very great many\ntimes; we may then be supposed to know for certain this\nfact (amongst many others) that in the long run head and\ntail will occur about equally often. But suppose we consider\nonly a moderate number of throws, or fewer still, and so\ncontinue limiting the number until we come down to three\nor two, or even one? We have, as the extreme cases, certainty\nor something undistinguishably near it, and utter\nuncertainty. Have we not, between these extremes, all\ngradations of belief? There is a large body of writers, including\nsome of the most eminent authorities upon this\nsubject, who state or imply that we are distinctly conscious of\nsuch a variation of the amount of our belief, and that this\nstate of our minds can be measured and determined with\nalmost the same accuracy as the external events to which\nthey refer. The principal mathematical supporter of this\nview is De Morgan, who has insisted strongly upon it in all\nhis works on the subject. The clearest exposition of his\nopinions will be found in his _Formal Logic_, in which work he\nhas made the view which we are now discussing the basis of\nhis system. He holds that we have a certain amount of belief\nof every proposition which may be set before us, an amount\nwhich in its nature admits of determination, though we may\npractically find it difficult in any particular case to determine\nit. He considers, in fact, that Probability is a sort of sister\nscience to Formal Logic,[1] speaking of it in the following\nwords: \"I cannot understand why the study of the effect,\nwhich partial belief of the premises produces with respect to\nthe conclusion, should be separated from that of the consequences\nof supposing the former to be absolutely true.\"[2]\nIn other words, there is a science--Formal Logic--which investigates\nthe rules according to which one proposition can be\nnecessarily inferred from another; in close correspondence\nwith this there is a science which investigates the rules according\nto which the amount of our belief of one proposition\nvaries with the amount of our belief of other propositions\nwith which it is connected.\n\nThe same view is also supported by another high authority,\nthe late Prof. Donkin, who says (_Phil. Mag._ May, 1851), \"It\nwill, I suppose, be generally admitted, and has often been\nmore or less explicitly stated, that the subject-matter of\ncalculation in the mathematical theory of Probabilities is\n_quantity of belief_.\"\n\n5. Before proceeding to criticise this opinion, one remark\nmay be made upon it which has been too frequently\noverlooked. It should be borne in mind that, even were this\nview of the subject not actually incorrect, it might be objected\nto as insufficient for the purpose of a definition, on the ground\nthat variation of belief is not confined to Probability. It is\na property with which that science is concerned, no doubt,\nbut it is a property which meets us in other directions as\nwell. In every case in which we extend our inferences by\nInduction or Analogy, or depend upon the witness of others,\nor trust to our own memory of the past, or come to a conclusion\nthrough conflicting arguments, or even make a long and\ncomplicated deduction by mathematics or logic, we have a\nresult of which we can scarcely feel as certain as of the premises\nfrom which it was obtained. In all these cases then\nwe are conscious of varying quantities of belief, but are the\nlaws according to which the belief is produced and varied the\nsame? If they cannot be reduced to one harmonious scheme,\nif in fact they can at best be brought to nothing but a number\nof different schemes, each with its own body of laws and rules,\nthen it is vain to endeavour to force them into one science.\n\nThis opinion is strengthened by observing that most of\nthe writers who adopt the definition in question do practically\ndismiss from consideration most of the above-mentioned\nexamples of diminution of belief, and confine their attention\nto classes of events which have the property discussed in\nChap I., viz. 'ignorance of the few, knowledge of the many.'\nIt is quite true that considerable violence has to be done to\nsome of these examples, by introducing exceedingly arbitrary\nsuppositions into them, before they can be forced to assume\na suitable form. But still there is little doubt that, if we\ncarefully examine the language employed, we shall find that\nin almost every case assumptions are made which virtually\nimply that our knowledge of the individual is derived from\npropositions given in the typical form described in Chap I.\nThis will be more fully proved when we come to consider\nsome common misapplications of the science.\n\n6. Even then, if the above-mentioned view of the\nsubject were correct, it would yet, I consider, be insufficient\nfor the purpose of a definition; but it is at least very doubtful\nwhether it is correct. Before we could properly assign to\nthe belief side of the question the prominence given to it by\nDe Morgan and others, certainly before the science could be\ndefined from that side, it would be necessary, it appears, to\nestablish the two following positions, against both of which\nstrong objections can be brought.\n\n(1) That our belief of every proposition is a thing which\nwe can, strictly speaking, be said to measure; that\nthere must be a certain amount of it in every case,\nwhich we can realize somehow in consciousness and\nrefer to some standard so as to pronounce upon its\nvalue.\n\n(2) That the value thus apprehended is the correct one\naccording to the theory, viz. that it is the exact\nfraction of full conviction that it should be. This\nstatement will perhaps seem somewhat obscure at\nfirst; it will be explained presently.\n\n7. (I.) Now, in the first place, as regards the difficulty\nof obtaining any measure of the amount of our belief. One\nsource of this difficulty is too obvious to have escaped notice;\nthis is the disturbing influence produced on the quantity of\nbelief by any strong emotion or passion. A deep interest in\nthe matter at stake, whether it excite hope or fear, plays great\nhavoc with the belief-meter, so that we must assume the\nmind to be quite unimpassioned in weighing the evidence.\nThis is noticed and acknowledged by Laplace and others;\nbut these writers seem to me to assume it to be the only\nsource of error, and also to be of comparative unimportance.\nEven if it were the only source of error I cannot see that it\nwould be unimportant. We experience hope or fear in so\nvery many instances, that to omit such influences from consideration\nwould be almost equivalent to saying that whilst\nwe profess to consider the whole quantity of our belief we\nwill in reality consider only a portion of it. Very strong\nfeelings are, of course, exceptional, but we should nevertheless\nfind that the emotional element, in some form or other,\nmakes itself felt on almost every occasion. It is very seldom\nthat we cannot speak of our surprise or expectation in reference\nto any particular event. Both of these expressions, but\nespecially the former, seem to point to something more than\nmere belief. It is true that the word 'expectation' is generally\ndefined in treatises on Probability as equivalent to\nbelief; but it seems doubtful whether any one who attends\nto the popular use of the terms would admit that they were\nexactly synonymous. Be this however as it may, the emotional\nelement is present upon almost every occasion, and its\ndisturbing influence therefore is constantly at work.\n\n8. Another cause, which co-operates with the former,\nis to be found in the extreme complexity and variety of the\nevidence on which our belief of any proposition depends.\nHence it results that our actual belief at any given moment\nis one of the most fugitive and variable things possible, so\nthat we can scarcely ever get sufficiently clear hold of it to\nmeasure it. This is not confined to the times when our\nminds are in a turmoil of excitement through hope or fear.\nIn our calmest moments we shall find it no easy thing to\ngive a precise answer to the question, How firmly do I hold\nthis or that belief? There may be one or two prominent\narguments in its favour, and one or two corresponding objections\nagainst it, but this is far from comprising all the\ncauses by which our state of belief is produced. Because\nsuch reasons as these are all that can be practically introduced\ninto oral or written controversies, we must not conclude\nthat it is by these only that our conviction is influenced.\nOn the contrary, our conviction generally rests upon a sort\nof chaotic basis composed of an infinite number of inferences\nand analogies of every description, and these moreover distorted\nby our state of feeling at the time, dimmed by the\ndegree of our recollection of them afterwards, and probably\nreceived from time to time with varying force according to\nthe way in which they happen to combine in our consciousness\nat the moment. To borrow a striking illustration from\nAbraham Tucker, the substructure of our convictions is not\nso much to be compared to the solid foundations of an ordinary\nbuilding, as to the piles of the houses of Rotterdam\nwhich rest somehow in a deep bed of soft mud. They bear\ntheir weight securely enough, but it would not be easy to\npoint out accurately the dependence of the different parts\nupon one another. Directly we begin to think of the amount\nof our belief, we have to think of the arguments by which it\nis produced--in fact, these arguments will intrude themselves\nwithout our choice. As each in turn flashes through the\nmind, it modifies the strength of our conviction; we are like\na person listening to the confused hubbub of a crowd, where\nthere is always something arbitrary in the particular sound\nwe choose to listen to. There may be reasons enough to\nsuffice abundantly for our ultimate choice, but on examination\nwe shall find that they are by no means apprehended\nwith the same force at different times. The belief produced\nby some strong argument may be very decisive at the moment,\nbut it will often begin to diminish when the argument\nis not actually before the mind. It is like being dazzled by\na strong light; the impression still remains, but begins almost\nimmediately to fade away. I think that this is the\ncase, however we try to limit the sources of our conviction.\n\n9. (II.) But supposing that it were possible to strike\na sort of average of this fluctuating state, should we find this\naverage to be of the amount assigned by theory? In other\nwords, is our natural belief in the happening of two different\nevents in direct proportion to the frequency with which those\nevents happen in the long run? There is a lottery with 100\ntickets and ten prizes; is a man's belief that he will get a\nprize fairly represented by one-tenth of certainty? The mere\nreference to a lottery should be sufficient to disprove this.\nLotteries have flourished at all times, and have never failed\nto be abundantly supported, in spite of the most perfect conviction,\non the part of many, if not of most, of those who put\ninto them, that in the long run all will lose. Deductions\nshould undoubtedly be made for those who act from superstitious\nmotives, from belief in omens, dreams, and so on.\nBut apart from these, and supposing any one to come fortified\nby all that mathematics can do for him, it is difficult to\nbelieve that his natural impressions about single events would\nbe always what they should be according to theory. Are\nthere many who can honestly declare that they would have\nno desire to buy a single ticket? They would probably say\nto themselves that the sum they paid away was nothing\nworth mentioning to lose, and that there was a chance of\ngaining a great deal; in other words, they are not apportioning\ntheir belief in the way that theory assigns.\n\nWhat bears out this view is, that the same persons who\nwould act in this way in single instances would often not\nthink of doing so in any but single instances. In other\nwords, the natural tendency here is to attribute too great an\namount of belief where it is or should be small; i.e. to depreciate\nthe risk in proportion to the contingent advantage.\nThey would very likely, when argued with, attach disparaging\nepithets to this state of feeling, by calling it an unaccountable\nfascination, or something of that kind, but of\nits existence there can be little doubt. We are speaking\nnow of what is the natural tendency of our minds, not of\nthat into which they may at length be disciplined by education\nand thought. If, however, educated persons have succeeded\nfor the most part in controlling this tendency in\ngames of chance, the spirit of reckless speculation has\nscarcely yet been banished from commerce. On examination,\nthis tendency will be found so prevalent in all ages, ranks,\nand dispositions, that it would be inadmissible to neglect it in\norder to bring our supposed instincts more closely into accordance\nwith the commonly received theories of Probability.\n\n10. There is another aspect of this question which has\nbeen often overlooked, but which seems to deserve some\nattention. Granted that we have an instinct of credence,\nwhy should it be assumed that this must be just of that intensity\nwhich subsequent experience will justify? Our\ninstincts are implanted in us for good purposes, and are intended\nto act immediately and unconsciously. They are,\nhowever, subject to control, and have to be brought into\naccordance with what we believe to be true and right. In\nother departments of psychology we do not assume that\nevery spontaneous prompting of nature is to be left just as\nwe find it, or even that on the average, omitting individual\nvariations, it is set at that pitch that will be found in the\nend to be the best when we come to think about it and assign\nits rules. Take, for example, the case of resentment. Here\nwe have an instinctive tendency, and one that on the whole\nis good in its results. But moralists are agreed that almost\nall our efforts at self-control are to be directed towards subduing\nit and keeping it in its right direction. It is assumed\nto be given as a sort of rough protection, and to be set, if\none might so express oneself, at too high a pitch to be\ndeliberately and consciously acted on in society. May not\nsomething of this kind be the case also with our belief?\nI only make a passing reference to this point here, as on\nthe theory of Probability adopted in this work it does not\nappear to be at all material to the science. But it seems\na strong argument against the expediency of commencing\nthe study of the science from the subjective side, or even of\nassigning any great degree of prominence to this side.\n\nThat men _do_ not believe in exact accordance with this\ntheory must have struck almost every one, but this has\nprobably been considered as mere exception and irregularity;\nthe assumption being made that on the average, and in far\nthe majority of cases, they do so believe. As stated above,\nit is very doubtful whether the tendency which has just\nbeen discussed is not so widely prevalent that it might with\nfar more propriety be called the rule than the exception.\nAnd it may be better that this should be so: many good\nresults may follow from that cheerful disposition which induces\na man sometimes to go on trying after some great\ngood, the chance of which he overvalues. He will keep on\nthrough trouble and disappointment, without serious harm\nperhaps, when the cool and calculating bystander sees plainly\nthat his 'measure of belief' is much higher than it should\nbe. So, too, the tendency also so common, of underrating\nthe chance of a great evil may also work for good. By many\nmen death might be looked upon as an almost infinite evil,\nat least they would so regard it themselves; suppose they\nkept this contingency constantly before them at its right\nvalue, how would it be possible to get through the practical\nwork of life? Men would be stopping indoors because if\nthey went out they might be murdered or bitten by a mad\ndog. To say this is not to advocate a return to our instincts;\nindeed when we have once reached the critical and conscious\nstate, it is hardly possible to do so; but it should be noticed\nthat the advantage gained by correcting them is at best but\na balanced one.[3] What is most to our present purpose, it\nsuggests the inexpediency of attempting to found an exact\ntheory on what may afterwards prove to be a mere instinct,\nunauthorized in its full extent by experience.\n\n11. It may be replied, that though people, as a matter\nof fact, do not apportion belief in this exact way, yet they\n_ought_ to do so. The purport of this remark will be examined\npresently; it need only be said here that it grants all that\nis now contended for. For it admits that the degree of our\nbelief is capable of modification, and may need it. But in\naccordance with what is the belief to be modified? obviously\nin accordance with experience; it cannot be trusted to by\nitself, but the fraction at which it is to be rated must be\ndetermined by the comparative frequency of the events to\nwhich it refers. Experience then furnishing the standard, it\nis surely most reasonable to start from this experience, and to\nfound the theory of our processes upon it.\n\nIf we do not do this, it should be observed that we are\ndetaching Probability altogether from the study of things\nexternal to us, and making it nothing else in effect than a\nportion of Psychology. If we refuse to be controlled by\nexperience, but confine our attention to the laws according\nto which belief is naturally or instinctively compounded and\ndistributed in our minds, we have no right then to appeal to\nexperience afterwards even for illustrations, unless under the\nexpress understanding that we do not guarantee its accuracy.\nOur belief in some single events, for example, might be correct,\nand yet that in a compound of several (if derived merely\nfrom our instinctive laws of belief) very possibly might not\nbe correct, but might lead us into practical mistakes if we\ndetermined to act upon it. Even if the two were in accordance,\nthis accordance would have to be proved, which would\nlead us round, by what I cannot but think a circuitous\nprocess, to the point which has been already chosen for\ncommencing with.\n\n12. De Morgan seems to imply that the doctrine\ncriticised above finds a justification from the analogy of\nFormal Logic. If the laws of necessary inference can be\nstudied apart from all reference to external facts (except\nby way of illustration), why not those of probable inference?\nThere does not, however, seem to be much force in any such\nanalogy. Formal Logic, at any rate under its modern or\nKantian mode of treatment, is based upon the assumption\nthat there are laws of thought as distinguished from laws of\nthings, and that these laws of thought can be ascertained and\nstudied without taking into account their reference to any\nparticular object. Now so long as we are confined to necessary\nor irreversible laws, as is of course the case in ordinary\nFormal Logic, this assumption leads to no special difficulties.\nWe mean by this, that no conflict arises between these subjective\nand objective necessities. The two exist in perfect\nharmony side by side, the one being the accurate counterpart\nof the other. So precise is the correspondence between\nthem, that few persons would notice, until study of metaphysics\nhad called their attention to such points, that there\nwere these two sides to the question. They would make\ntheir appeal to either with equal confidence, saying indifferently,\n'the thing must be so,' or, 'we cannot conceive its being\notherwise.' In fact it is only since the time of Kant that\nthis mental analysis has been to any extent appreciated and\naccepted. And even now the dominant experience school of\nphilosophy would not admit that there are here two really\ndistinct sides to the phenomenon; they maintain either that\nthe subjective necessity is nothing more than the consequence\nby inveterate association of the objective uniformity,\nor else that this so-called necessity (say in the Law of Contradiction)\nis after all merely verbal, merely a different way of\nsaying the same thing over again in other words. Whatever\nthe explanation adopted, the general result is that fallacies,\nas real acts of thought, are impossible within the domain of\npure logic; error within that province is only possibly by a\nmomentary lapse of attention, that is of consciousness.\n\n13. But though this perfect harmony between subjective\nand objective uniformities or laws may exist within\nthe domain of pure logic, it is far from existing within that\nof probability. The moment we make the _quantity_ of our\nbelief an integral part of the subject to be studied, any such\ninvariable correspondence ceases to exist. In the former\ncase, we could not consciously think erroneously even though\nwe might try to do so; in the latter, we not only can believe\nerroneously but constantly do so. Far from the quantity of\nour belief being so exactly adjusted in conformity with the\nfacts to which it refers that we cannot even in imagination\ngo astray, we find that it frequently exists in excess or defect\nof that which subsequent judgment will approve. Our instincts\nof credence are unquestionably in frequent hostility\nwith experience; and what do we do then? We simply\nmodify the instincts into accordance with the things. We\nare constantly performing this practice, and no cultivated\nmind would find it possible to do anything else. No man\nwould think of divorcing his belief from the things on which\nit was exercised, or would suppose that the former had anything\nelse to do than to follow the lead of the latter. Hence\nit results that that separation of the subjective necessity from\nthe objective, and that determination to treat the former\nas a science apart by itself, for which a plausible defence\ncould be made in the case of pure logic, is entirely inadmissible\nin the case of probability. However we might\ncontrive to '_think_' aright without appeal to facts, we cannot\n_believe_ aright without incessantly checking our proceedings\nby such appeals. Whatever then may be the\nclaims of Formal Logic to rank as a separate science, it\ndoes not appear that it can furnish any support to the\ntheory of Probability at present under examination.\n\n14. The point in question is sometimes urged as\nfollows. Suppose a man with two, and only two, alternatives\nbefore him, one of which he knows must involve\nsuccess and the other failure. He knows nothing more\nabout them than this, and he is forced to act. Would he\nnot regard them with absolutely similar and equal feelings\nof confidence, without the necessity of referring them to any\nreal or imaginary series? If so, is not this equivalent to\nsaying that his belief of either, since one of them must\ncome to pass, is equal to that of the other, and therefore that\nhis belief of each is one-half of full confidence? Similarly\nif there are more than two alternatives: let it be supposed\nthat there are any number of them, amongst which no\ndistinctions whatever can be discerned except in such particulars\nas we know for certain will not affect the result;\nshould we not feel equally confident in respect of each of\nthem? and so here again should we riot have a fractional\nestimate of our absolute amount of belief? It is thus\nattempted to lay the basis of a pure science of Probability,\ndetermining the distribution and combination of our belief\nhypothetically; viz. _if_ the contingencies are exactly alike,\nthen our belief is so apportioned, the question whether the\ncontingencies are equal being of course decided as the objective\ndata of Logic or Mathematics are decided.\n\nTo discuss this question fully would require a statement\nat some length of the reasons in favour of the objective or\nmaterial view of Logic, as opposed to the Formal or Conceptualist.\nI shall have to speak on this subject in another\nchapter, and will not therefore enter upon it here. But one\nconclusive objection which is applicable more peculiarly to\nProbability may be offered at once. To pursue the line of\nenquiry just indicated, is, as already remarked, to desert\nthe strictly logical ground, and to take up that appropriate\nto psychology; the proper question, in all these cases, being\nnot what _do_ men believe, but what ought they to believe?\nAdmitting, as was done above, that in the case of Formal\nLogic these two enquiries, or rather those corresponding to\nthem, practically run into one, owing to the fact that men\ncannot consciously 'think' wrongly; it cannot be too strongly\ninsisted on that in Probability the two are perfectly separable\nand distinct. It is of no use saying what men do or\nwill believe, we want to know what they will be right in\nbelieving; and this can never be settled without an appeal\nto the phenomena themselves.\n\n15. But apart from the above considerations, this way\nof putting the case does not seem to me at all conclusive.\nTake the following example. A man[4] finds himself on the\nsands of the Wash or Morecambe Bay, in a dense mist, when\nthe spring-tide is coming in; and knows therefore that to\nbe once caught by the tide would be fatal. He hears a\nchurch-bell at a distance, but has no means of knowing\nwhether it is on the same side of the water with himself or\non the opposite side. He cannot tell therefore whether by\nfollowing its sound he will be led out into the mid-stream\nand be lost, or led back to dry land and safety. Here there\ncan be no repetition of the event, and the cases are indistinguishably\nalike, to him, in the only circumstances which\ncan affect the issue: is not then his prospect of death, it\nwill be said, necessarily equal to one-half? A proper analysis\nof his state of mind would be a psychological rather than\na logical enquiry, and in any case, as above remarked, the\ndecision of this question does not touch our logical position.\nBut according to the best introspection I can give I should\nsay that what really passes through the mind in such a case\nis something of this kind: In most doubtful positions and\ncircumstances we are accustomed to decide our conduct by\na consideration of the relative advantages and disadvantages\nof each side, that is by the observed or inferred frequency\nwith which one or the other alternative has succeeded. In\nproportion as these become more nearly balanced, we are\nmore frequently mistaken in the individual cases; that is, it\nbecomes more and more nearly what would be called 'a\nmere toss up' whether we are right or wrong. The case\nin question seems merely the limiting case, in which it has\nbeen contrived that there shall be no appreciable difference\nbetween the alternatives, by which to decide in favour of\none or other, and we accordingly feel no confidence in the\nparticular result. Having to decide, however, we decide according\nto the precedent of similar cases which have occurred\nbefore. To stand still and wait for better information is\ncertain death, and we therefore appeal to and employ the\nonly rule we know of; or rather we feel, or endeavour to\nfeel, as we have felt before when acting in the presence of\nalternatives as nearly balanced as possible. But I can\nneither perceive in my own case, nor feel convinced in that\nof others, that this appeal, in a case which cannot be repeated,[5]\nto a rule acted on and justified in cases which can be\nand are repeated, at all forces us to admit that our state of\nmind is the same in each case.\n\n16. This example serves to bring out very clearly a point\nwhich has been already mentioned, and which will have to be\ninsisted upon again, viz. that all which Probability discusses\nis the statistical frequency of events, or, if we prefer so to\nput it, the quantity of belief with which any one of these\nevents should be individually regarded, but leaves all the\nsubsequent conduct dependent upon that frequency, or that\nbelief, to the choice of the agents. Suppose there are two\ntravellers in the predicament in question: shall they keep\ntogether, or separate in opposite directions? In either case\nalike the chance of safety to each is the same, viz. one-half,\nbut clearly their circumstances must decide which course it\nis preferable to adopt. If they are husband and wife, they will\nprobably prefer to remain together; if they are sole depositaries\nof an important state secret, they may decide to part.\nIn other words, we have to select here between the two alternatives\nof the certainty of a single loss, and the even chance\nof a double loss; alternatives which the common mathematical\nstatement of their chances has a decided tendency\nto make us regard as indistinguishable from one another.\nBut clearly the decision must be grounded on the desires,\nfeelings, and conscience of the agents. Probability cannot\nsay a word upon this question. As I have pointed out elsewhere,\nthere has been much confusion on this matter in\napplications of the science to betting, and in the discussion\nof the Petersburg problem.\n\nWe have thus examined the doctrine in question with\na minuteness which may seem tedious, but in consequence of\nthe eminence of its supporters it would have been presumptuous\nto have rejected it without the strongest grounds. The\nobjections which have been urged might be summarised as\nfollows:--the amount of our belief of any given proposition,\nsupposing it to be in its nature capable of accurate determination\n(which does not seem to be the case), depends upon a\ngreat variety of causes, of which statistical frequency--the\nsubject of Probability--is but one. That even if we confine\nour attention to this one cause, the natural amount of our\nbelief is not necessarily what theory would assign, but has to\nbe checked by appeal to experience. The subjective side of\nProbability therefore, though very interesting and well deserving\nof examination, seems a mere appendage of the objective,\nand affords in itself no safe ground for a science of\ninference.\n\n17. The conception then of the science of Probability\nas a science of the laws of belief seems to break down at\nevery point. We must not however rest content with such\nmerely negative criticism. The degree of belief we entertain\nof a proposition may be hard to get at accurately, and\nwhen obtained may be often wrong, and may need therefore\nto be checked by an appeal to the objects of belief. Still in\npopular estimation we do seem to be able with more or less\naccuracy to form a graduated scale of intensity of belief.\nWhat we have to examine now is whether this be possible,\nand, if so, what is the explanation of the fact?\n\nThat it is generally believed that we can form such a\nscale scarcely admits of doubt. There is a whole vocabulary\nof common expressions such as, 'I feel almost sure,' 'I do not\nfeel quite certain,' 'I am less confident of this than of that,'\nand so on. When we make use of any one of these phrases\nwe seldom doubt that we have a distinct meaning to convey\nby means of it. Nor do we feel much at a loss, under any\ngiven circumstances, as to which of these expressions we\nshould employ in preference to the others. If we were asked\nto arrange in order, according to the intensity of the belief\nwith which we respectively hold them, things broadly marked\noff from one another, we could do it from our consciousness\nof belief alone, without a fresh appeal to the evidence upon\nwhich the belief depended. Passing over the looser propositions\nwhich are used in common conversation, let us take but\none simple example from amongst those which furnish numerical\ndata. Do I not feel more certain that some one will die\nthis week in the whole town, than in the particular street in\nwhich I live? and if the town is known to contain a population\none hundred times greater than that in the street, would\nnot almost any one be prepared to assert on reflection that\nhe felt a hundred times more sure of the first proposition\nthan of the second? Or to take a non-numerical example, are\nwe not often able to say unhesitatingly which of two propositions\nwe believe the most, and to some rough degree how\nmuch more we believe one than the other, at a time when all\nthe evidence upon which each rests has faded from the\nmind, so that each has to be judged, as we may say, solely on\nits own merits?\n\nHere then a problem proposes itself. If popular opinion,\nas illustrated in common language, be correct,--and very\nconsiderable weight must of course be attributed to it,--there\ndoes exist something which we call partial belief in reference\nto any proposition of the numerical kind described\nabove. Now what we want to do is to find some test or\njustification of this belief, to obtain in fact some intelligible\nanswer to the question, Is it correct? We shall find incidentally\nthat the answer to this question will throw a good deal\nof light upon another question nearly as important and far\nmore intricate, viz. What is the meaning of this partial belief?\n\n18. We shall find it advisable to commence by ascertaining\nhow such enquiries as the above would be answered\nin the case of ordinary full belief. Such a step would not\noffer the slightest difficulty. Suppose, to take a simple\nexample, that we have obtained the following proposition,--whether\nby induction, or by the rules of ordinary deductive\nlogic, does not matter for our present purpose,--that a certain\nmixture of oxygen and hydrogen is explosive. Here we have\nan inference, and consequent belief of a proposition. Now\nsuppose there were any enquiry as to whether our belief\nwere correct, what should we do? The simplest way of\nsettling the matter would be to find out by a distinct appeal\nto experience whether the proposition was true. Since we\nare reasoning about things, the justification of the belief, that\nis, the test of its correctness, would be most readily found in\nthe truth of the proposition. If by any process of inference\nI have come to believe that a certain mixture will explode, I\nconsider my belief to be justified, that is to be correct, if\nunder proper circumstances the explosion always does occur;\nif it does not occur the belief was wrong.\n\nSuch an answer, no doubt, goes but a little way, or rather\nno way at all, towards explaining what is the nature of belief\nin itself; but it is sufficient for our present purpose, which is\nmerely that of determining what is meant by the correctness\nof our belief, and by the test of its correctness. In all inferences\nabout things, in which the _amount_ of our belief is not\ntaken into account, such an explanation as the above is quite\nsufficient; it would be the ordinary one in any question of\nscience. It is moreover perfectly intelligible, whether the\nconclusion is particular or universal. Whether we believe\nthat 'some men die', or that 'all men die', our belief may with\nequal ease be tested by the appropriate train of experience.\n\n19. But when we attempt to apply the same test to\n_partial_ belief, we shall find ourselves reduced to an awkward\nperplexity. A difficulty now emerges which has been singularly\noverlooked by those who have treated of the subject.\nAs a simple example will serve our purpose, we will take the\ncase of a penny. I am about to toss one up, and I therefore\nhalf believe, to adopt the current language, that it will give\nhead. Now it seems to be overlooked that if we appeal to\nthe event, as we did in the case last examined, our belief\nmust inevitably be wrong, and therefore the test above mentioned\nwill fail. For the thing must either happen or not\nhappen: i.e. in this case the penny must either give head, or\nnot give it; there is no third alternative. But whichever\nway it occurs, our half-belief, so far as such a state of mind\nadmits of interpretation, must be wrong. If head does come,\nI am wrong in not having expected it enough; for I only half\nbelieved in its occurrence. If it does not happen, I am\nequally wrong in having expected it too much; for I half\nbelieved in its occurrence, when in fact it did not occur at all.\n\nThe same difficulty will occur in every case in which we\nattempt to justify our state of partial belief in a single contingent\nevent. Let us take another example, slightly differing\nfrom the last. A man is to receive \u00a31 if a die gives six,\nto pay 1_s_. if it gives any other number. It will generally be\nadmitted that he ought to give 2_s_. 6_d_. for the chance, and\nthat if he does so he will be paying a fair sum. This example\nonly differs from the last in the fact that instead of\nsimple belief in a proposition, we have taken what mathematicians\ncall 'the _value_ of the expectation'. In other words,\nwe have brought into a greater prominence, not merely the belief,\nbut the conduct which is founded upon the belief. But\nprecisely the same difficulty recurs here. For appealing to the\nevent,--the single event, that is,--we see that one or other\nparty must lose his money without compensation. In what\nsense then can such an expectation be said to be a fair one?\n\n20. A possible answer to this, and so far as appears the\nonly possible answer, will be, that what we really mean by\nsaying that we half believe in the occurrence of head is to\nexpress our conviction that head will certainly happen on\nthe average every other time. And similarly, in the second\nexample, by calling the sum a fair one it is meant that in\nthe long run neither party will gain or lose. As we shall\nrecur presently to the point raised in this form of answer, the\nonly notice that need be taken of it at this point is to call\nattention to the fact that it entirely abandons the whole\nquestion in dispute, for it admits that this partial belief does\nnot in any strict sense apply to the individual event, since it\nclearly cannot be justified there. At such a result indeed we\ncannot be surprised; at least we cannot on the theory adopted\nthroughout this Essay. For bearing in mind that the employment\nof Probability postulates ignorance of the single\nevent, it is not easy to see how we are to justify any other\nopinion or statement about the single event than a confession\nof such ignorance.\n\n21. So far then we do not seem to have made the\nslightest approximation to a solution of the particular\nquestion now under examination. The more closely we have\nanalysed special examples, the more unmistakeably are we\nbrought to the conclusion that in the individual instance no\njustification of anything like quantitative belief is to be\nfound; at least none is to be found in the same sense in\nwhich we expect it in ordinary scientific conclusions, whether\nInductive or Deductive. And yet we have to face and\naccount for the fact that common impressions, as attested by\na whole vocabulary of common phrases, are in favour of the\nexistence of this quantitative belief. How are we to account\nfor this? If we appeal to an example again, and analyse it\nsomewhat more closely, we may yet find our way to some\nsatisfactory explanation.\n\nIn our previous analysis (\u00a718) we found it sufficient to stop\nat an early stage, and to give as the justification of our belief\nthe fact of the proposition being true. Stopping however at\nthat stage, we have found this explanation fail altogether to\ngive a justification of partial belief; fail, that is, when applied\nto the individual instance. The two states of belief and disbelief\ncorrespond admirably to the two results of the event\nhappening and not happening respectively, and unless for\npsychological purposes we saw no reason to analyse further;\nbut to partial belief there is nothing corresponding in the result,\nfor the event cannot partially happen in such cases as we\nare concerned with. Suppose then we advance a step further\nin the analysis, and ask again what is meant by the proposition\nbeing true? This introduces us, of course, to a very long\nand intricate path; but in the short distance along it which\nwe shall advance, we shall not, it is to be hoped, find any\nvery serious difficulty. As before, we will illustrate the\nanalysis by first applying it to the case of ordinary full belief.\n\n22. Whatever opinion then may be held about the\nessential nature of belief, it will probably be admitted that a\nreadiness to act upon the proposition believed is an inseparable\naccompaniment of that state of mind. There can be no\nalteration in our belief (at any rate in the case of sane persons)\nwithout a possible alteration in our conduct, nor anything in\nour conduct which is not connected with something in our\nbelief. We will first take an example in connection with the\npenny, in which there is full belief; we will analyse it a step\nfurther than we did before, and then attempt to apply the\nsame analysis to an example of a similar kind, but one in\nwhich the belief is partial instead of full.\n\nSuppose that I am about to throw a penny up, and contemplate\nthe prospect of its falling upon one of its sides and\nnot upon its edge. We feel perfectly confident that it will\ndo so. Now whatever else may be implied in our belief, we\ncertainly mean this; that we are ready to stake our conduct\nupon its falling thus. All our betting, and everything else\nthat we do, is carried on upon this supposition. Any risk\nwhatever that might ensue upon its falling otherwise will be\nincurred without fear. This, it must be observed, is equally\nthe case whether we are speaking of a single throw or of a\nlong succession of throws.\n\nBut now let us take the case of a penny falling, not upon\none side or the other, but upon a given side, _head_. To a\ncertain extent this example resembles the last. We are perfectly\nready to stake our conduct upon what comes to pass in\nthe long run. When we are considering the result of a large\nnumber of throws, we are ready to act upon the supposition\nthat head comes every other time. If e.g. we are betting\nupon it, we shall not object to paying \u00a31 every time that\nhead comes, on condition of receiving \u00a31 every time that\nhead does not come. This is nothing else than the _translation_,\nas we may call it, into practice, of our belief that head\nand tail occur equally often.\n\nNow it will be obvious, on a moment's consideration, that\nour conduct is capable of being slightly varied: of being\nvaried, that is, in form, whilst it remains identical in respect\nof its results. It is clear that to pay \u00a31 every time we lose,\nand to get \u00a31 every time we gain, comes to precisely the same\nthing, in the case under consideration, as to pay ten shillings\nevery time without exception, and to receive \u00a31 every time\nthat head occurs. It is so, because heads occur, on the\naverage, every other time. In the long run the two results\ncoincide; but there is a marked difference between the two\ncases, considered individually. The difference is two-fold.\nIn the first place we depart from the notion of a payment\nevery other time, and come to that of one made every time.\nIn the second place, what we pay every time is half of what\nwe get in the cases in which we do get anything. The difference\nmay seem slight; but mark the effect when our conduct\nis translated back again into the subjective condition\nupon which it depends, viz. into our belief. It is in consequence\nof such a translation, as it appears to me, that the\nnotion has been acquired that we have an accurately determinable\namount of belief as to every such proposition. To\nhave losses and gains of equal amount, and to incur them\nequally often, was the experience connected with our belief\nthat the two events, head and tail, would occur equally often.\nThis was quite intelligible, for it referred to the long run.\nTo find that this could be commuted for a payment made\nevery time without exception, a payment, observe, of half the\namount of what we occasionally receive, has very naturally\nbeen interpreted to mean that there must be a state of half-belief\nwhich refers to each individual throw.\n\n23. One such example, of course, does not go far towards\nestablishing a theory. But the reader will bear in\nmind that almost all our conduct tends towards the same\nresult; that it is not in betting only, but in every course of\naction in which we have to count the events, that such a\nnumerical apportionment of our conduct is possible. Hence,\nby the ordinary principles of association, it would appear\nexceedingly likely that, not exactly a numerical condition of\nmind, but rather numerical associations, become inseparably\nconnected with each particular event which we know to occur\nin a certain proportion of times. Once in six times a die\ngives ace; a knowledge of this fact, taken in combination\nwith all the practical results to which it leads, produces, one\ncannot doubt, an inseparable notion of one-sixth connected\nwith each _single_ throw. But it surely cannot be called belief\nto the amount of one-sixth; at least it admits neither of\njustification nor explanation in these single cases, to which\nalone the fractional belief, if such existed, ought to apply.\n\nIt is in consequence, I apprehend, of such association that\nwe act in such an unhesitating manner in reference to any\nsingle contingent event, even when we have no expectation\nof its being repeated. A die is going to be thrown up once,\nand once only. I bet 5 to 1 against ace, not, as is commonly\nasserted, because I feel one-sixth part of certainty in the\noccurrence of ace; but because I know that such conduct\nwould be justified in the long run of such cases, and I apply\nto the solitary individual the same rule that I should apply\nto it if I knew it were one of a long series. This accounts\nfor my conduct being the same in the two cases; by association,\nmoreover, we probably experience very similar feelings\nin regard to them both.\n\n24. And here, on the view of the subject adopted in\nthis Essay, we might stop. We are bound to explain the\n'measure of our belief' in the occurrence of a single event\nwhen we judge solely from the statistical frequency with\nwhich such events occur, for such a series of events was our\nstarting-point; but we are not bound to inquire whether in\nevery case in which persons have, or claim to have, a certain\nmeasure of belief there must be such a series to which to\nrefer it, and by which to justify it. Those who start from\nthe subjective side, and regard Probability as the science of\nquantitative belief, are obliged to do this, but we are free\nfrom the obligation.\n\nStill the question is one which is so naturally raised in\nconnection with this subject, that it cannot be altogether\npassed by. I think that to a considerable extent such a\njustification as that mentioned above will be found applicable\nin other cases. The fact is that we are very seldom called\nupon to decide and act upon a single contingency which cannot\nbe viewed as being one of a series. Experience introduces\nus, it must be remembered, not merely to a succession\nof events neatly arranged in a single series (as we have\nhitherto assumed them to be for the purpose of illustration),\nbut to an infinite number belonging to a vast variety of\ndifferent series. A man is obliged to be acting, and therefore\nexercising his belief about one thing or another, almost\nthe whole of every day of his life. Any one person will have\nto decide in his time about a multitude of events, each one\nof which may never recur again within his own experience.\nBut by the very fact of there being a multitude, though they\nare all of different kinds, we shall still find that order is\nmaintained, and so a course of conduct can be justified. In\na plantation of trees we should find that there is order of a\ncertain kind if we measure them in any one direction, the\ntrees being on an average about the same distance from each\nother. But a somewhat similar order would be found if we\nwere to examine them in any other direction whatsoever. So\nin nature generally; there is regularity in a succession of\nevents of the same kind. But there may also be regularity\nif we form a series by taking successively a number out of\ntotally distinct kinds.\n\nIt is in this circumstance that we find an extension of the\npractical justification of the measure of our belief. A man,\nsay, buys a life annuity, insures his life on a railway journey,\nputs into a lottery, and so on. Now we may make a series\nout of these acts of his, though each is in itself a single event\nwhich he may never intend to repeat. His conduct, and therefore\nhis belief, measured by the result in each individual\ninstance, will not be justified, but the reverse, as shown in \u00a719.\nCould he indeed repeat each kind of action often\nenough it would be justified; but from this, by the conditions\nof life, he is debarred. Now it is perfectly conceivable that\nin the new series, formed by his successive acts of different\nkinds, there should be no regularity. As a matter of fact,\nhowever, it is found that there is regularity. In this way the\nequalization of his gains and losses, for which he cannot hope\nin annuities, insurances, and lotteries taken separately, may\nyet be secured to him out of these events taken collectively.\nIf in each case he values his chance at its right proportion\n(and acts accordingly) he will in the course of his life neither\ngain nor lose. And in the same way if, whenever he has the\nalternative of different courses of conduct, he acts in accordance\nwith the estimate of his belief described above, i.e.\nchooses the event whose chance is the best, he will in the end\ngain more in this way than by any other course. By the existence,\ntherefore, of these _cross-series_, as we may term them,\nthere is an immense addition to the number of actions which\nmay be fairly considered to belong to those courses of conduct\nwhich offer many successive opportunities of equalizing\ngains and losses. All these cases then may be regarded as\nadmitting of justification in the way now under discussion.\n\n25. In the above remarks it will be observed that we\nhave been giving what is to be regarded as a justification of\nhis belief from the point of view of the individual agent himself.\nIf we suppose the existence of an enlarged fellow-feeling,\nthe applicability of such a justification becomes still more\nextensive. We can assign a very intelligible sense to the\nassertion that it is 999 to 1 that I shall not get a prize in a\nlottery, even if this be stated in the form that my belief in\nmy so doing is represented by the fraction 1/1000th of certainty.\nProperly it means that in a very large number of throws I\nshould gain once in 1000 times. If we include other contingencies\nof the same kind, as described in the last section,\neach individual may be supposed to reach to something like\nthis experience within the limits of his own life. He could\nnot do it in this particular line of conduct alone, but he could\ndo it in this line combined with others. Now introduce the\npossibility of each man feeling that the gain of others offers\nsome analogy to his own gains, which we may conceive his\ndoing except in the case of the gains of those against whom\nhe is directly competing, and the above justification becomes\nstill more extensively applicable.\n\nThe following would be a fair illustration to test this\nview. I know that I must die on some day of the week, and\nthere are but seven days. My belief, therefore, that I shall\ndie on a Sunday is one-seventh. Here the contingent event\nis clearly one that does not admit of repetition; and yet\nwould not the belief of every man have the value assigned it\nby the formula? It would appear that the same principle\nwill be found to be at work here as in the former examples.\nIt is quite true that I have only the opportunity of dying\nonce myself, but I am a member of a class in which deaths\noccur with frequency, and I form my opinion upon evidence\ndrawn from that class. If, for example, I had insured my\nlife for \u00a31000, I should feel a certain propriety in demanding\n\u00a37000 in case the office declared that it would only pay in\nthe event of my dying on a Sunday. _I_, indeed, for my own\nprivate part, might not find the arrangement an equitable\none; but mankind at large, in case they acted on such a\nprinciple, might fairly commute their aggregate gains in such\na way, whilst to the Insurance Office it would not make any\ndifference at all.\n\n26. The results of the last few sections might be summarised\nas follows:--the different amounts of belief which\nwe entertain upon different events, and which are recognized\nby various phrases in common use, have undoubtedly some\nmeaning. But the greater part of their meaning, and certainly\ntheir only justification, are to be sought in the _series_\nof corresponding events to which they belong; in regard to\nwhich it may be shown that far more events are capable of\nbeing referred to a series than might be supposed at first\nsight. The test and justification of belief are to be found in\nconduct; in this test applied to the series as a whole, there\nis nothing peculiar, it differs in no way from the similar test\nwhen we are acting on our belief about any single event.\nBut so applied, from the nature of the case it is applied\nsuccessively to each of the individuals of the series; here our\n_conduct_ generally admits of being separately considered in\nreference to each particular event; and this has been understood\nto denote a certain amount of belief which should be a\nfraction of certainty. Probably on the principles of association,\na peculiar condition of mind is produced in reference to\neach single event. And these associations are not unnaturally\nretained even when we contemplate any one of these single\nevents isolated from any series to which it belongs. When\nit is found alone we treat it, and feel towards it, as we do\nwhen it is in company with the rest of the series.\n\n27. We may now see, more clearly than we could\nbefore, why it is that we are free from any necessity of assuming\nthe existence of causation, in the sense of necessary\ninvariable sequence, in the case of the events which compose\nour series. Against such a view it might very plausibly be\nurged, that we constantly talk of the probability of a single\nevent; but how can this be done, it may reasonably be said,\nif we once admit the possibility of that event occurring fortuitously?\nTake an instance from human life; the average\nduration of the lives of a batch of men aged thirty will be\nabout thirty-four years. We say therefore to any individual\nof them, Your expectation of life is thirty-four years. But\nhow can this be said if we admit that the train of events\ncomposing his life is liable to be destitute of all regular\nsequence of cause and effect? To this it may be replied\nthat the denial of causation enables us to say neither more\nnor less than its assertion, in reference to the length of the\nindividual life, for of this we are ignorant in each case alike.\nBy assigning, as above, an expectation in reference to the\nindividual, we _mean_ nothing more than to make a statement\nabout the average of his class. Whether there be causation\nor not in these individual cases does not affect our knowledge\nof the average, for this by supposition rests on independent\nexperience. The legitimate inferences are the same on either\nhypothesis, and of equal value. The only difference is that\non the hypothesis of non-causation we have forced upon our\nattention the impropriety of talking of the 'proper' expectation\nof the individual, owing to the fact that all knowledge of\nits amount is formally impossible; on the other hypothesis\nthe impropriety is overlooked from the fact of such knowledge\nbeing only practically unattainable. As a matter of\nfact the amount of our knowledge is the same in each case;\nit is a knowledge of the average, and of that only.[6]\n\n28. We may conclude, then, that the limits within\nwhich we are thus able to justify the amount of our belief\nare far more extensive than might appear at first sight.\nWhether every case in which persons feel an amount of\nbelief short of perfect confidence could be forced into the\nprovince of Probability is a wider question. Even, however,\nif the belief could be supposed capable of justification on its\nprinciples, its rules could never in such cases be made use of.\nSuppose, for example, that a father were in doubt whether\nto give a certain medicine to his sick child. On the one\nhand, the doctor declared that the child would die unless the\nmedicine were given; on the other, through a mistake, the\nfather cannot feel quite sure that the medicine he has is the\nright one. It is conceivable that some mathematicians, in\ntheir conviction that everything has its definite numerical\nprobability, would declare that the man's belief had some\n'value' (if they could only find out what it is), say nine-tenths;\nby which they would mean that in nine cases out of\nten in which he entertained a belief of that particular value\nhe proved to be right. So with his belief and doubt on\nthe other side of the question. Putting the two together,\nthere is but one course which, as a prudent man and a good\nfather, he can possibly follow. It may be so, but when (as\nhere) the identification of an event in a series depends on\npurely subjective conditions, as in this case upon the degree\nof vividness of his conviction, of which no one else can judge,\nno test is possible, and therefore no proof can be found.\n\n29. So much then for the attempts, so frequently\nmade, to found the science on a subjective basis; they can\nlead, as it has here been endeavoured to show, to no satisfactory\nresult. Still our belief is so inseparably connected with\nour action, that something of a defence can be made for the\nattempts described above; but when it is attempted, as is\noften the case, to import other sentiments besides pure belief,\nand to find a justification for them also in the results of our\nscience, the confusion becomes far worse. The following\nextract from Archbishop Thomson's _Laws of Thought_ (\u00a7122,\nEd. II.) will show what kind of applications of the science are\ncontemplated here: \"In applying the doctrine of chances to\nthat subject in connexion with which it was invented--games\nof chance,--the principles of what has been happily termed\n'moral arithmetic' must not be forgotten. Not only would\nit be difficult for a gamester to find an antagonist on terms,\nas to fortune and needs, precisely equal, but also it is impossible\nthat with such an equality the advantage of a\nconsiderable gain should balance the harm of a serious loss.\n'If two men,' says Buffon, 'were to determine to play for\ntheir whole property, what would be the effect of this agreement?\nThe one would only double his fortune, and the\nother reduce his to naught. What proportion is there between\nthe loss and the gain? The same that there is between\nall and nothing. The gain of the one is but a moderate\nsum,--the loss of the other is numerically infinite, and\nmorally so great that the labour of his whole life may not\nperhaps suffice to restore his property.'\"\n\nAs moral advice this is all very true and good. But if it\nbe regarded as a contribution to the science of the subject it\nis quite inappropriate, and seems calculated to cause confusion.\nThe doctrine of chances pronounces upon certain\nkinds of events in respect of number and magnitude; it has\nabsolutely nothing to do with any particular person's feelings\nabout these relations. We might as well append a corollary\nto the rules of arithmetic, to point out that although it is\nvery true that twice two are four it does not follow that four,\nhorses will give twice as much pleasure to the owner as two\nwill. If two men play on equal terms their chances are\nequal; in other words, if they were often to play in this\nmanner each would lose as frequently as he would gain. That\nis all that Probability can say; what under the circumstances\nmay be the determination and opinions of the men in question,\nit is for them and them alone to decide. There are\nmany persons who cannot bear mediocrity of any kind, and\nto whom the prospect of doubling their fortune would outweigh\na greater chance of losing it altogether. They alone\nare the judges.\n\nIf we will introduce such a balance of pleasure and pain\nthe individual must make the calculation for himself. The\nsupposition is that total ruin is very painful, partial loss\npainful in a less proportion than that assigned by the ratio\nof the losses themselves; the inference is therefore drawn\nthat on the average more pain is caused by occasional great\nlosses than by frequent small ones, though the money value\nof the losses in the long run may be the same in each case.\nBut if we suppose a country where the desire of spending\nlargely is very strong, and where owing to abundant production\nloss is easily replaced, the calculation might incline the\nother way. Under such circumstances it is quite possible\nthat more happiness might result from playing for high than\nfor low stakes. The fact is that all emotional considerations\nof this kind are irrelevant; they are, at most, mere applications\nof the theory, and such as each individual is alone\ncompetent to make for himself. Some more remarks will be\nmade upon this subject in the chapter upon Insurance and\nGambling.\n\n30. It is by the introduction of such considerations as\nthese that the Petersburg Problem has been so perplexed.\nHaving already given some description of this problem we\nwill refer to it very briefly here. It presents us with a\nsequence of sets of throws for each of which sets I am to\nreceive something, say a shilling, as the minimum receipt.\nMy receipts increase in proportion to the rarity of each\nparticular kind of set, and each kind is observed or inferred\nto grow more rare in a certain definite but unlimited order.\nBy the wording of the problem, properly interpreted, I am\nsupposed never to stop. Clearly therefore, however large a\nfee I pay for each of these sets, I shall be sure to make it up\nin time. The mathematical expression of this is, that I\nought always to pay an infinite sum. To this the objection\nis opposed, that no sensible man would think of advancing\neven a large finite sum, say \u00a350. Certainly he would not;\nbut why? Because neither he nor those who are to pay\nhim would be likely to live long enough for him to obtain\nthrows good enough to remunerate him for one-tenth of his\noutlay; to say nothing of his trouble and loss of time. We\nmust not suppose that the problem, as stated in the ideal\nform, will coincide with the practical form in which it\npresents itself in life. A carpenter might as well object to\nEuclid's second postulate, because his plane came to a stop\nin six feet on the plank on which he was at work. Many\npersons have failed to perceive this, and have assumed that,\nbesides enabling us to draw numerical inferences about the\nmembers of a series, the theory ought also to be called upon\nto justify all the opinions which average respectable men\nmight be inclined to form about them, as well as the conduct\nthey might choose to pursue in consequence. It is obvious\nthat to enter upon such considerations as these is to diverge\nfrom our proper ground. We are concerned, in these cases,\nwith the actions of men only, as given in statistics; with the\nemotions they experience in the performance of these actions\nwe have no direct concern whatever. The error is the same\nas if any one were to confound, in political economy, value in\nuse with value in exchange, and object to measuring the\nvalue of a loaf by its cost of production, because bread is\nworth more to a man when he is hungry than it is just after\nhis dinner.\n\n31. One class of emotions indeed ought to be excepted,\nwhich, from the apparent uniformity and consistency\nwith which they show themselves in different persons\nand at different times, do really present some better claim to\nconsideration. In connection with a science of inference\nthey can never indeed be regarded as more than an accident\nof what is essential to the subject, but compared with other\nemotions they seem to be inseparable accidents.\n\nThe reader will remember that attention was drawn in\nthe earlier part of this chapter to the compound nature of\nthe state of mind which we term belief. It is partly intellectual,\npartly also emotional; it professes to rest upon\nexperience, but in reality the experience acts through the\ndistorting media of hopes and fears and other disturbing\nagencies. So long as we confine our attention to the _state\nof mind_ of the person who believes, it appears to me that\nthese two parts of belief are quite inseparable. Indeed, to\nspeak of them as two parts may convey a wrong impression;\nfor though they spring from different sources, they so entirely\nmerge in one result as to produce what might be\ncalled an indistinguishable compound. Every kind of inference,\nwhether in probability or not, is liable to be disturbed\nin this way. A timid man may honestly believe that he will\nbe wounded in a coming battle, when others, with the same\nexperience but calmer judgments, see that the chance is\ntoo small to deserve consideration. But such a man's belief,\nif we look only to that, will not differ in its nature from\nsound belief. His conduct also in consequence of his belief\nwill by itself afford no ground of discrimination; he will\nmake his will as sincerely as a man who is unmistakeably on\nhis death-bed. The only resource is to check and correct\nhis belief by appealing to past and current experience.[7] This\nwas advanced as an objection to the theory on which probability\nis regarded as concerned primarily with laws of belief.\nBut on the view taken in this Essay in which we are supposed\nto be concerned with laws of inference about things,\nerror and difficulty from this source vanish. Let us bear clearly\nin mind that we are concerned with inferences about things,\nand whatever there may be in belief which does not depend\non experience will disappear from notice.\n\n32. These emotions then can claim no notice as an\nintegral portion of any science of inference, and should in\nstrictness be rigidly excluded from it. But if any of them\nare uniform and regular in their production and magnitude,\nthey may be fairly admitted as accidental and extraneous\naccompaniments. This is really the case to some extent\nwith our surprise. This emotion does show a considerable\ndegree of uniformity. The rarer any event is the more am I,\nin common with most other men, surprised at it when it does\nhappen. This surprise may range through all degrees, from\nthe most languid form of interest up to the condition which\nwe term 'being startled'. And since the surprise seems\nto be pretty much the same, under similar circumstances,\nat different times, and in the case of different persons, it is\nfree from that extreme irregularity which is found in most\nof the other mental conditions which accompany the contemplation\nof unexpected events. Hence our surprise, though,\nas stated above, having no proper claim to admission into\nthe science of Probability, is such a constant and regular\naccompaniment of that which Probability is concerned with,\nthat notice must often be taken of it. References will occasionally\nbe found to this aspect of the question in the\nfollowing chapters.\n\nIt may be remarked in passing, for the sake of further\nillustration of the subject, that this emotional accompaniment\nof surprise, to which we are thus able to assign something\nlike a fractional value, differs in two important respects\nfrom the commonly accepted fraction of belief. In the first\nplace, it has what may be termed an independent existence;\nit is intelligible by itself. The belief, as we endeavoured to\nshow, needs explanation and finds it in our consequent conduct.\nNot so with the emotion; this stands upon its own\nfooting, and may be examined in and by itself. Hence, in\nthe second place, it is as applicable, and as capable of any kind\nof justification, in relation to the _single event_, as to a series of\nevents. In this respect, as will be remembered, it offers a\ncomplete contrast to our state of belief about any one contingent\nevent. May not these considerations help to account\nfor the general acceptance of the doctrine, that we have a\ncertain definite and measurable amount of belief about these\nevents? I cannot help thinking that what is so obviously\ntrue of the emotional portion of the belief, has been unconsciously\ntransferred to the other or intellectual portion of the\ncompound condition, to which it is not applicable, and where\nit cannot find a justification.\n\n33. A further illustration may now be given of the\nsubjective view of Probability at present under discussion.\n\nAn appeal to common language is always of service, as\nthe employment of any distinct word is generally a proof\nthat mankind have observed some distinct properties in the\nthings, which have caused them to be singled out and have\nthat name appropriated to them. There is such a class of\nwords assigned by popular usage to the kind of events of\nwhich Probability takes account. If we examine them we\nshall find, I think, that they direct us unmistakeably to the\ntwo-fold aspect of the question,--the objective and the subjective,\nthe quality in the events and the state of our minds\nin considering them,--that have occupied our attention\nduring the former chapters.\n\nThe word 'extraordinary', for instance, seems to point to\nthe observed fact, that events are arranged in a sort of _ordo_\nor rank. No one of them might be so exactly placed that\nwe could have inferred its position, but when we take a great\nmany into account together, running our eye, as it were,\nalong the line, we begin to see that they really do for the\nmost part stand in order. Those which stand away from the\nline have this divergence observed, and are called extraordinary,\nthe rest ordinary, or in the line. So too 'irregular'\nand 'abnormal' are doubtless used from the appearance\nof things, when examined in large numbers, being that\nof an arrangement by rule or measure. This only holds\nwhen there are a good many; we could not speak of the\nsingle events being so arranged. Again the word 'law', in\nits philosophical sense, has now become quite popularised.\nHow the term became introduced is not certain, but\nthere can be little doubt that it was somewhat in this\nway:--The effect of a law, in its usual application to\nhuman conduct, is to produce regularity where it did not\npreviously exist; when then a regularity began to be perceived\nin nature, the same word was used, whether the cause\nwas supposed to be the same or not. In each case there\nwas the same generality of agreement, subject to occasional\ndeflection.[8]\n\nOn the other hand, observe the words 'wonderful', 'unexpected',\n'incredible'. Their connotation describes states\nof mind simply; they are of course not confined to Probability,\nin the sense of statistical frequency, but imply simply\nthat the events they denote are such as from some cause we\ndid not expect would happen, and at which therefore, when\nthey do happen, we are surprised.\n\nNow when we bear in mind that these two classes of\nwords are in their origin perfectly distinct;--the one denoting\nsimply events of a certain character; the other,\nthough also denoting events, _connoting_ simply states of\nmind;--and yet that they are universally applied to the\nsame events, so as to be used as perfectly synonymous, we\nhave in this a striking illustration of the two sides under\nwhich Probability may be viewed, and of the universal recognition\nof a close connection between them. The words are\npopularly used as synonymous, and we must not press their\nmeaning too far; but if it were to be observed, as I am\nrather inclined to think it could, that the application of the\nwords which denote mental states is wider than that of the\nothers, we should have an illustration of what has been\nalready observed, viz. that the province of Probability is not\nso extensive as that over which variation of belief might be\nobserved. Probability only considers the case in which this\nvariation is brought about in a certain definite statistical\nway.\n\n34. It will be found in the end both interesting and\nimportant to have devoted some attention to this subjective\nside of the question. In the first place, as a mere speculative\ninquiry the quantity of our belief of any proposition\ndeserves notice. To study it at all deeply would be to trespass\ninto the province of Psychology, but it is so intimately\nconnected with our own subject that we cannot avoid all\nreference to it. We therefore discuss the laws under which\nour expectation and surprise at isolated events increases or\ndiminishes, so as to account for these states of mind in any\nindividual instance, and, if necessary, to correct them when\nthey vary from their proper amount.\n\nBut there is another more important reason than this.\nIt is quite true that when the subjects of our discussion in\nany particular instance lie entirely within the province\nof Probability, they may be treated without any reference\nto our belief. We may or we may not employ this side of\nthe question according to our pleasure. If, for example, I\nam asked whether it is more likely that A. B. will die this\nyear, than that it will rain to-morrow, I may calculate the\nchance (which really is at bottom the same thing as my\nbelief) of each, find them respectively, one-sixth and one-seventh,\nsay, and therefore decide that my 'expectation' of\nthe former is the greater, viz. that this is the more likely\nevent. In this case the process is precisely the same whether\nwe suppose our belief to be introduced or not; our mental\nstate is, in fact, quite immaterial to the question. But, in\nother cases, it may be different. Suppose that we are comparing\ntwo things, of which one is wholly alien to Probability,\nin the sense that it is hopeless to attempt to assign\nany degree of numerical frequency to it, the only ground\nthey have in common may be the amount of belief to which\nthey are respectively entitled. We cannot compare the\nfrequency of their occurrence, for one may occur too seldom\nto judge by, perhaps it may be unique. It has been already\nsaid, that our belief of many events rests upon a very complicated\nand extensive basis. My belief may be the product\nof many conflicting arguments, and many analogies more or\nless remote; these proofs themselves may have mostly faded\nfrom my mind, but they will leave their effect behind them\nin a weak or strong conviction. At the time, therefore, I\nmay still be able to say, with some degree of accuracy,\nthough a very slight degree, what amount of belief I entertain\nupon the subject. Now we cannot compare things that\nare heterogeneous: if, therefore, we are to decide between\nthis and an event determined naturally and properly by\nProbability, it is impossible to appeal to chances or frequency\nof occurrence. The measure of belief is the only common\nground, and we must therefore compare this quantity in each\ncase. The test afforded will be an exceedingly rough one,\nfor the reasons mentioned above, but it will be better than\nnone; in some cases it will be found to furnish all we want.\n\nSuppose, for example, that one letter in a million is lost\nin the Post Office, and that in any given instance I wish to\nknow which is more likely, that a letter has been so lost, or\nthat my servant has stolen it? If the latter alternative\ncould, like the former, be stated in a numerical form, the\ncomparison would be simple. But it cannot be reduced to\nthis form, at least not consciously and directly. Still, if we\ncould feel that our belief in the man's dishonesty was greater\nthan one-millionth, we should then have homogeneous things\nbefore us, and therefore comparison would be possible.\n\n35. We are now in a position to give a tolerably accurate\ndefinition of a phrase which we have frequently been\nobliged to employ, or incidentally to suggest, and of which\nthe reader may have looked for a definition already, viz. the\nprobability of an event, or what is equivalent to this, the\nchance of any given event happening. I consider that these\nterms presuppose a series; within the indefinitely numerous\nclass which composes this series a smaller class is distinguished\nby the presence or absence of some attribute or\nattributes, as was fully illustrated and explained in a previous\nchapter. These larger and smaller classes respectively\nare commonly spoken of as instances of the 'event,' and of\n'its happening in a given particular way.' Adopting this\nphraseology, which with proper explanations is suitable\nenough, we may define the probability or chance (the terms\nare here regarded as synonymous) of the event happening\nin that particular way as the numerical fraction which represents\nthe proportion between the two different classes in the\nlong run. Thus, for example, let the probability be that\nof a given infant living to be eighty years of age. The\nlarger series will comprise all infants, the smaller all who live\nto eighty. Let the proportion of the former to the latter be\n9 to 1; in other words, suppose that one infant in ten lives\nto eighty. Then the chance or probability that any given\ninfant will live to eighty is the numerical fraction 1/10. This\nassumes that the series are of indefinite extent, and of the\nkind which we have described as possessing a fixed type.\nIf this be not the case, but the series be supposed terminable,\nor regularly or irregularly fluctuating, as might be the\ncase, for instance, in a society where owing to sanitary or\nother causes the average longevity was steadily undergoing\na change, then in so far as this is the case the series ceases\nto be a subject of science. What we have to do under these\ncircumstances, is to substitute a series of the right kind for\nthe inappropriate one presented by nature, choosing it, of\ncourse, with as little deflection as possible from the observed\nfacts. This is nothing more than has to be done, and invariably\nis done, whenever natural objects are made subjects\nof strict science.\n\n36. A word or two of explanation may be added about\nthe expression employed above, 'the proportion in the long\nrun.' The run must be supposed to be very long indeed, in\nfact never to stop. As we keep on taking more terms of the\nseries we shall find the proportion still fluctuating a little,\nbut its fluctuations will grow less. The proportion, in fact,\nwill gradually approach towards some fixed numerical value,\nwhat mathematicians term its _limit_. This fractional value\nis the one spoken of above. In the cases in which deductive\nreasoning is possible, this fraction may be obtained without\ndirect appeal to statistics, from reasoning about the conditions\nunder which the events occur, as was explained in\nthe fourth chapter.\n\nHere becomes apparent the full importance of the distinction\nso frequently insisted on, between the actual irregular\nseries before us and the substituted one of calculation, and\nthe meaning of the assertion (Ch. I. \u00a713), that it was in the\ncase of the latter only that strict scientific inferences could\nbe made. For how can we have a 'limit' in the case of\nthose series which ultimately exhibit irregular fluctuations?\nWhen we say, for instance, that it is an even chance that\na given person recovers from the cholera, the meaning of\nthis assertion is that in the long run one half of the persons\nattacked by that disease do recover. But if we examined\na sufficiently extensive range of statistics, we might find\nthat the manners and customs of society had produced such\na change in the type of the disease or its treatment, that we\nwere no nearer approaching towards a fixed limit than we\nwere at first. The conception of an ultimate limit in the\nratio between the numbers of the two classes in the series\nnecessarily involves an absolute fixity of the type. When\ntherefore nature does not present us with this absolute fixity,\nas she seldom or never does except in games of chance (and\nnot demonstrably there), our only resource is to introduce\nsuch a series, in other words, as has so often been said, to\nsubstitute a series of the right kind.\n\n37. The above, which may be considered tolerably\ncomplete as a definition, might equally well have been\ngiven in the last chapter. It has been deferred however\nto the present place, in order to connect with it at once a\nproposition involving the conceptions introduced in this\nchapter; viz. the state of our own minds, in reference to the\namount of belief we entertain in contemplating any one\nof the events whose probability has just been described.\nReasons were given against the opinion that our belief admitted\nof any exact apportionment like the numerical one\njust mentioned. Still, it was shown that a reasonable explanation\ncould be given of such an expression as, 'my belief is\n1/10th of certainty', though it was an explanation which pointed\nunmistakeably to a series of events, and ceased to be intelligible,\nor at any rate justifiable, when it was not viewed in\nsuch a relation to a series. In so far, then, as this explanation\nis adopted, we may say that our belief is in proportion\nto the above fraction. This referred to the purely\nintellectual part of belief which cannot be conceived to be\nseparable, even in thought, from the things upon which it\nis exercised. With this intellectual part there are commonly\nassociated various emotions. These we can to a\ncertain extent separate, and, when separated, can measure\nwith that degree of accuracy which is possible in the case of\nother emotions. They are moreover intelligible in reference\nto the individual events. They will be found to increase\nand diminish in accordance, to some extent, with the fraction\nwhich represents the scarcity of the event. The emotion of\nsurprise does so with some degree of accuracy.\n\nThe above investigation describes, though in a very brief\nform, the amount of truth which appears to me to be contained\nin the assertion frequently made, that the fraction\nexpressive of the probability represents also the fractional\npart of full certainty to which our belief of the individual\nevent amounts. Any further analysis of the matter would\nseem to belong to Psychology rather than to Probability.\n\n\n1. In the ordinary signification of this term. As De Morgan uses it he\n  makes Formal Logic _include_ Probability, as one of its branches, as\n  indicated in his title \"Formal Logic, or the Calculus of Inference,\n  necessary and probable.\"\n\n2. _Formal Logic_. Preface, page v.\n\n3. An illustration of the points here insisted on has recently [1876]\n  been given in a quarter where few would have expected it; I allude,\n  as many readers will readily infer, to J. S. Mill's exceedingly\n  interesting Essays on Theism. It is not within our province here to\n  criticise any of their conclusions, but they have expressed in a\n  very significant way the conviction entertained by him that beliefs\n  which are not justified by evidence, and possibly may not be capable\n  of justification (those for instance of immortality and the\n  existence of the Deity), may nevertheless not only continue to exist\n  in cultivated minds, but may also be profitably encouraged there, at\n  any rate in the shape of hopes, for certain supposed advantages\n  attendant on their retention, irrespective even of their truth.\n\n4. It is necessary to take an example in which the man is forced to\n  act, or we should not be able to shew that he has any belief on the\n  subject at all. He may declare that he neither knows nor cares\n  anything about the matter, and that therefore there is nothing of\n  the nature of belief to be extracted out of his mental condition. He\n  very likely would take this ground if we asked him, as De Morgan\n  does, with a slightly different reference (_Formal Logic_, p. 183),\n  whether he considers that there are volcanoes on the unseen side of\n  the moon larger than those on the side turned towards us; or, with\n  Jevons (_Principles of Science_, Ed. II. p. 212) whether he\n  considers that a Platythliptic Coefficient is positive. These do not\n  therefore seem good instances to illustrate the position that we\n  always entertain a certain degree of belief on every question which\n  can be stated, and that utter inability to give a reason in favour\n  of either alternative corresponds to half belief.\n\n5. Except indeed on the principles indicated further on in \u00a7\u00a724, 25.\n\n6. For a fuller discussion of this, see the Chapter on Causation.\n\n7. The best example I can recall of the distinction between judging\n  from the subjective and the objective side, in such cases as these,\n  occurred once in a railway train. I met a timid old lady who was in\n  much fear of accidents. I endeavoured to soothe her on the usual\n  statistical ground of the extreme rarity of such events. She\n  listened patiently, and then replied, \"Yes, Sir, that is all very\n  well; but I don't see how the real danger will be a bit the less\n  because I don't believe in it.\"\n\n8. This would still hold of _empirical_ laws which may be capable of\n  being broken: we now have very much shifted the word, to denote an\n  _ultimate_ law which it is supposed cannot be broken.\n\n\n\n\nCHAPTER VII.\n\n\n_THE RULES OF INFERENCE IN PROBABILITY._\n\n1. In the previous chapter, an investigation was made into\nwhat may be called, from the analogy of Logic, Immediate\nInferences. Given that nine men out of ten, of any assigned\nage, live to forty, what could be inferred about the prospect\nof life of any particular man? It was shown that, although\nthis step was very far from being so simple as it is frequently\nsupposed to be, and as the corresponding step really is in\nLogic, there was nevertheless an intelligible sense in which\nwe might speak of the amount of our belief in any one of\nthese 'proportional propositions,' as they may succinctly be\ntermed, and justify that amount. We must now proceed to\nthe consideration of inferences more properly so called, I\nmean inferences of the kind analogous to those which form the\nstaple of ordinary logical treatises. In other words, having\nascertained in what manner particular propositions could be\ninferred from the general propositions which included them,\nwe must now examine in what cases one general proposition\ncan be inferred from another. By a general proposition here\nis meant, of course, a general proposition of the statistical\nkind contemplated in Probability. The rules of such inference\nbeing very few and simple, their consideration will not\ndetain us long. From the data now in our possession we are\nable to deduce the rules of probability given in ordinary\ntreatises upon the science. It would be more correct to say\nthat we are able to deduce _some_ of these rules, for, as will\nappear on examination, they are of two very different kinds,\nresting on entirely distinct grounds. They might be divided\ninto those which are formal, and those which are more or less\nexperimental. This may be otherwise expressed by saying\nthat, from the kind of series described in the first chapters,\nsome rules will follow necessarily by the mere application of\narithmetic; whilst others either depend upon peculiar hypotheses,\nor demand for their establishment continually renewed\nappeals to experience, and extension by the aid of the\nvarious resources of Induction. We shall confine our attention\nat present principally to the former class; the latter can\nonly be fully understood when we have considered the connection\nof our science with Induction.\n\n2. The fundamental rules of Probability strictly so\ncalled, that is the formal rules, may be divided into two\nclasses,--those obtained by addition or subtraction on the\none hand, corresponding to what are generally termed the\nconnection of exclusive or incompatible events;[1] and those\nobtained by multiplication or division, on the other hand,\ncorresponding to what are commonly termed dependent\nevents. We will examine these in order.\n\n(1) We can make inferences by simple addition. If,\nfor instance, there are two distinct properties observable in\nvarious members of the series, which properties do not occur\nin the same individual; it is plain that in any batch the\nnumber that are of one kind or the other will be equal to the\nsum of those of the two kinds separately. Thus 36.4 infants\nin 100 live to over sixty, 35.4 in 100 die before they are\nten;[2] take a large number, say 10,000, then there will be\nabout 3640 who live to over sixty, and about 3540 who do\nnot reach ten; hence the total number who do not die within\nthe assigned limits will be about 2820 altogether. Of course\nif these proportions were accurately assigned, the resultant\nsum would be equally accurate: but, as the reader knows, in\nProbability this proportion is merely the limit towards which\nthe numbers tend in the long run, not the precise result\nassigned in any particular case. Hence we can only venture\nto say that this is the limit towards which we tend as the\nnumbers become greater and greater.\n\nThis rule, in its general algebraic form, would be expressed\nin the language of Probability as follows:--If the\nchances of two exclusive or incompatible events be respectively\n1/m and 1/n the chance of one or other of them\nhappening will be 1/m + 1/n or (m + n)/mn. Similarly if there were\nmore than two events of the kind in question. On the principles\nadopted in this work, the rule, when thus algebraically\nexpressed, means precisely the same thing as when it is\nexpressed in the statistical form. It was shown at the conclusion\nof the last chapter that to say, for example, that the\nchance of a given event happening in a certain way is 1/6, is\nonly another way of saying that in the long run it does tend\nto happen in that way once in six times.\n\nIt is plain that a sort of corollary to this rule might be\nobtained, in precisely the same way, by subtraction instead of\naddition. Stated generally it would be as follows:--If the\nchance of one or other of two incompatible events be 1/m and\nthe chance of one alone be 1/n, the chance of the remaining\none will be 1/m - 1/n or (n - m)/nm.\n\nFor example, if the chance of any one dying in a year is 1/10,\nand his chance of dying of some particular disease is 1/100,\nhis chance of dying of any other disease is 9/100.\n\nThe reader will remark here that there are two apparently\ndifferent modes of stating this rule, according as we speak\nof 'one or other of two or more events happening,' or of 'the\nsame event happening in one or other of two or more ways.'\nBut no confusion need arise on this ground; either way of\nspeaking is legitimate, the difference being merely verbal,\nand depending (as was shown in the first chapter, \u00a78) upon\nwhether the distinctions between the 'ways' are or are not\ntoo deep and numerous to entitle the event to be conventionally\nregarded as the same.\n\nWe may also here point out the justification for the common\ndoctrine that certainty is represented by unity, just as\nany given degree of probability is represented by its appropriate\nfraction. If the statement that an event happens once\nin m times, is equivalently expressed by saying that its chance\nis 1/m, it follows that to say that it happens m times in m times,\nor every time without exception, is equivalent to\nsaying that its chance is m/m or 1. Now an event that happens\nevery time is of course one of whose occurrence we are\ncertain; hence the fraction which represents the 'chance' of\nan event which is certain becomes unity.\n\nIt will be equally obvious that given that the chance that\nan event will happen is 1/m, the chance that it will not happen\nis 1 - 1/m or (m - 1)/m.\n\n3. (2) We can also make inferences by multiplication\nor division. Suppose that two events instead of being\nincompatible, are connected together in the sense that one\nis contingent upon the occurrence of the other. Let us be\ntold that a given proportion of the members of the series\npossess a certain property, and a given proportion again of\nthese possess another property, then the proportion of the\nwhole which possess both properties will be found by multiplying\ntogether the two fractions which represent the above\ntwo proportions. Of the inhabitants of London, twenty-five\nin a thousand, say, will die in the course of the year; we\nsuppose it to be known also that one death in five is due to\nfever; we should then infer that one in 200 of the inhabitants\nwill die of fever in the course of the year. It would of course\nbe equally simple, by division, to make a sort of converse\ninference. Given the total mortality per cent. of the population\nfrom fever, and the proportion of fever cases to the\naggregate of other cases of mortality, we might have inferred,\nby dividing one fraction by the other, what was the total\nmortality per cent. from all causes.\n\nThe rule as given above is variously expressed in the\nlanguage of Probability. Perhaps the simplest and best\nstatement is that it gives us the rule of dependent events.\nThat is; if the chance of one event is 1/m, and the chance that\nif it happens another will also happen 1/n, then the chance\nof the latter is 1/mn. In this case it is assumed that the latter\nis so entirely dependent upon the former that though it does\nnot always happen with it, it certainly will not happen without\nit; the necessity of this assumption however may be\nobviated by saying that what we are speaking of in the\nlatter case is the _joint_ event, viz. both together if they are\nsimultaneous events, or the latter _in consequence of_ the\nformer, if they are successive.\n\n4. The above inferences are necessary, in the sense in\nwhich arithmetical inferences are necessary, and they do not\ndemand for their establishment any arbitrary hypothesis.\nWe assume in them no more than is warranted, and in fact\nnecessitated by the data actually given to us, and make our\ninferences from these data by the help of arithmetic. In the\nsimple examples given above nothing is required beyond\narithmetic in its most familiar form, but it need hardly be\nadded that in practice examples may often present themselves\nwhich will require much profounder methods than\nthese. It may task all the resources of that higher and more\nabstract arithmetic known as algebra to extract a solution.\nBut as the necessity of appeal to such methods as these does\nnot touch the principles of this part of the subject we need\nnot enter upon them here.\n\n5. The formula next to be discussed stands upon a\nsomewhat different footing from the above in respect of its\ncogency and freedom from appeal to experience, or to hypothesis.\nIn the two former instances we considered cases in\nwhich the data were supposed to be given under the conditions\nthat the properties which distinguished the different kinds of\nevents whose frequency was discussed, were respectively\nknown to be disconnected and known to be connected. Let\nus now suppose that no such conditions are given to us.\nOne man in ten, say, has black hair, and one in twelve\nis short-sighted; what conclusions could we then draw as\nto the chance of any given man having one only of these\ntwo attributes, or neither, or both? It is clearly possible\nthat the properties in question might be inconsistent with\none another, so as never to be found combined in the same\nperson; or all the short-sighted might have black hair; or\nthe properties might be allotted[3] in almost any other proportion\nwhatever. If we are perfectly ignorant upon these\npoints, it would seem that no inferences whatever could be\ndrawn about the required chances.\n\nInferences however _are_ drawn, and practically, in most\ncases, quite justly drawn. An escape from the apparent\nindeterminateness of the problem, as above described, is\nfound by assuming that, not merely will one-tenth of the\nwhole number of men have black hair (for this was given as\none of the data), but also that one-tenth alike of those who\nare and who are not short-sighted have black hair. Let us\ntake a batch of 1200, as a sample of the whole. Now, from\nthe data which were originally given to us, it will easily be\nseen that in every such batch there will be on the average\n120 who have black hair, and therefore 1080 who have not.\nAnd here in strict right we ought to stop, at least until we\nhave appealed again to experience; but we do not stop here.\nFrom data which we assume, we go on to infer that of the 120,\n10 (i.e. one-twelfth of 120) will be short-sighted, and\n110 (the remainder) will not. Similarly we infer that of the 1080,\n90 are short-sighted, and 990 are not. On the whole,\nthen, the 1200 are thus divided:--black-haired short-sighted, 10;\nshort-sighted without black hair, 90; black-haired men\nwho are not short-sighted, 110; men who are neither short-sighted\nnor have black hair, 990.\n\nThis rule, expressed in its most general form, in the\nlanguage of Probability, would be as follows:--If the chances\nof a thing being p and q are respectively 1/m and 1/n, then the\nchance of its being both p and q is 1/mn, p and not q is (n - 1)/mn,\nq and not p is (m - 1)/mn, not p and not q is ((m - 1)(n - 1))/mn,\nwhere p and q are independent. The sum of these chances\nis obviously unity; as it ought to be, since one or other of\nthe four alternatives must necessarily exist.\n\n6. I have purposely emphasized the distinction between\nthe inference in this case, and that in the two preceding,\nto an extent which to many readers may seem unwarranted.\nBut it appears to me that where a science makes\nuse, as Probability does, of two such very distinct sources of\nconviction as the necessary rules of arithmetic and the\nmerely more or less cogent ones of Induction, it is hardly\npossible to lay too much stress upon the distinction. Few\nwill be prepared to deny that very arbitrary assumptions\nhave been made by many writers on the subject, and none\nwill deny that in the case of what are called 'inverse probabilities'\nassumptions are sometimes made which are at least\ndecidedly open to question. The best course therefore is to\nmake a pause and stringent enquiry at the point at which the\npossibility of such error and doubtfulness first exhibits itself.\nThese remarks apply to some of the best writers on the subject;\nin the case of inferior writers, or those who appeal to\nProbability without having properly mastered its principles,\nwe may go further. It would really not be asserting too\nmuch to say that they seem to think themselves justified in\nassuming that where we know nothing about the distribution\nof the properties alluded to we must assume them to be distributed\nas above described, and therefore apportion our\nbelief in the same ratio. This is called 'assuming the events\nto be independent,' the supposition being made that the rule\nwill certainly follow from this independence, and that we\nhave a right, if we know nothing to the contrary, to assume\nthat the events are independent.\n\nThe validity of this last claim has already been discussed\nin the first chapter; it is only another of the attempts to\nconstruct _\u00e0 priori_ the series which experience will present to\nus, and one for which no such strong defence can be made as\nfor the equality of heads and tails in the throws of a penny.\nBut the meaning to be assigned to the 'independence' of the\nevents in question demands a moment's consideration.\n\nThe circumstances of the problem are these. There are\ntwo different qualities, by the presence and absence respectively\nof each of which, amongst the individuals of a series,\ntwo distinct pairs of classes of these individuals are produced.\nFor the establishment of the rule under discussion\nit was found that one supposition was both necessary and\nsufficient, namely, that the division into classes caused by\neach of the above distinctions should subdivide each of the\nclasses created by the other distinction in the same ratio\nin which it subdivides the whole. If the independence be\ngranted and so defined as to mean this, the rule of course\nwill stand, but, without especial attention being drawn to\nthe point, it does not seem that the word would naturally\nbe so understood.\n\n7. The above, then, being the fundamental rules of\ninference in probability, the question at once arises, What is\ntheir relation to the great body of formul\u00e6 which are made\nuse of in treatises upon the science, and in practical applications\nof it? The reply would be that these formul\u00e6, in so\nfar as they properly belong to the science, are nothing else\nin reality than applications of the above fundamental rules.\nSuch applications may assume any degree of complexity, for\nowing to the difficulty of particular examples, in the form in\nwhich they actually present themselves, recourse must sometimes\nbe made to the profoundest theorems of mathematics.\nStill we ought not to regard these theorems as being anything\nelse than convenient and necessary abbreviations of\narithmetical processes, which in practice have become too\ncumbersome to be otherwise performed.\n\nThis explanation will account for some of the rules as\nthey are ordinarily given, but by no means for all of them.\nIt will account for those which are demonstrable by the certain\nlaws of arithmetic, but not for those which in reality\nrest only upon inductive generalizations. And it can hardly\nbe doubted that many rules of the latter description have\nbecome associated with those of the former, so that in popular\nestimation they have been blended into one system, of\nwhich all the separate rules are supposed to possess a similar\norigin and equal certainty. Hints have already been frequently\ngiven of this tendency, but the subject is one of\nsuch extreme importance that a separate chapter (that on\nInduction) must be devoted to its consideration.\n\n8. In establishing the validity of the above rules, we\nhave taken as the basis of our investigations, in accordance\nwith the general scheme of this work, the statistical frequency\nof the events referred to; but it was also shown that each\nformula, when established, might with equal propriety be expressed\nin the more familiar form of a fraction representing\nthe 'chance' of the occurrence of the particular event. The\nquestion may therefore now be raised, Can those writers who\n(as described in the last chapter) take as the primary subject\nof the science not the degree of statistical frequency, but the\nquantity of belief, with equal consistency make this the basis\nof their rules, and so also regard the fraction expressive of\nthe chance as a merely synonymous expression? De Morgan\nmaintains that whereas in ordinary logic we suppose the\npremises to be absolutely true, the province of Probability is\nto study 'the effect which partial belief of the premises produces\nwith respect to the conclusion.' It would appear\ntherefore as if in strictness we ought on this view to be able\nto determine this consequent diminution at first hand, from\nintrospection of the mind, that is of the conceptions and\nbeliefs which it entertains; instead of making any recourse\nto statistics to tell us how much we ought to believe the\nconclusion.\n\nAny readers who have concurred with me in the general\nresults of the last chapter, will naturally agree in the conclusion\nthat nothing deserving the name of logical science can\nbe extracted from any results of appeal to our consciousness\nas to the quantity of belief we entertain of this or that proposition.\nSuppose, for example, that one person in 100 dies\non the sea passage out to India, and that one in 9 dies during\na 5 years residence there. It would commonly be said\nthat the chance that any one, who is now going out, has of\nliving to start homewards 5 years hence, is 88/100; for his chance\nof getting there is 99/100; and of his surviving, if he gets\nthere, 8/9; hence the result or dependent event is got by\nmultiplying these fractions together, which gives 88/100. Here\nthe real basis of the reasoning is statistical, and the processes\nor results are merely translated afterwards into fractions.\nBut can we say the same when we look at the belief side of\nthe question? I quite admit the psychological fact that we\nhave degrees of belief, more or less corresponding to the\nfrequency of the events to which they refer. In the above example,\nfor instance, we should undoubtedly admit on enquiry\nthat our belief in the man's return was affected by each of\nthe risks in question, so that we had less expectation of it\nthan if he were subject to either risk separately; that is, we\nshould in some way compound the risks. But what I cannot\nrecognise is that we should be able to perform the process\nwith any approach to accuracy without appeal to the statistics,\nor that, even supposing we could do so, we should\nhave any guarantee of the correctness of the result without\nsimilar appeal. It appears to me in fact that but little\nmeaning, and certainly no security, can be attained by so\nregarding the process of inference. The probabilities expressed\nas degrees of belief, just as those which are expressed\nas fractions, must, when we are put upon our justification,\nfirst be translated into their corresponding facts of statistical\nfrequency of occurrence of the events, and then the inferences\nmust be drawn and justified there. This part of\nthe operation, as we have already shown, is mostly carried\non by the ordinary rules of arithmetic. When we have\nobtained our conclusion we may, if we please, translate it\nback again into the subjective form, just as we can and do\nfor convenience into the fractional, but I do not see how the\nprocess of inference can be conceived as taking place in that\nform, and still less how any proof of it can thus be given. If\ntherefore the process of inference be so expressed it must be\nregarded as a symbolical process, symbolical of such an inference\nabout things as has been described above, and it\ntherefore seems to me more advisable to state and expound\nit in this latter form.\n\n\n_On Inverse Probability and the Rules required for it._\n\n9. It has been already stated that the only fundamental\nrules of inference in Probability are the two described\nin \u00a7\u00a72, 3, but there are of course abundance of derivative\nrules, the nature and use of which are best obtained from the\nstudy of any manual upon the subject. One class of these\nderivative rules, however, is sufficiently distinct in respect of\nthe questions to which it may give rise, to deserve special\nexamination. It involves the distinction commonly recognised\nas that between Direct and Inverse Probability. It is\nthus introduced by De Morgan:--\n\n\"In the preceding chapter we have calculated the chances\nof an event, knowing the circumstances under which it is to\nhappen or fail. We are now to place ourselves in an inverted\nposition: we know the event, and ask what is the probability\nwhich results from the event in favour of any set of circumstances\nunder which the same might have happened.\"[4] The\ndistinction might therefore be summarily described as that\nbetween finding an effect when we are given the causes, and\nfinding a cause when we are given effects.\n\nOn the principles of the science involved in the definition\nwhich was discussed and adopted in the earlier chapters of\nthis work, the reader will easily infer that no such distinction\nas this can be regarded as fundamental. One common feature\nwas traced in all the objects which were to be referred to\nProbability, and from this feature the possible rules of\ninference can be immediately derived. All other distinctions\nare merely those of arrangement or management.\n\nBut although the distinction is not by any means fundamental,\nit is nevertheless true that the practical treatment\nof such problems as those principally occurring in Inverse\nProbability, does correspond to a very serious source of\nambiguity and perplexity. The arbitrary assumptions which\nappear in Direct Probability are not by any means serious,\nbut those which invade us in a large proportion of the problems\noffered by Inverse Probability are both serious and\ninevitable.\n\n10. This will be best seen by the examination of\nspecial examples; as any, however simple, will serve our\npurpose, let us take the two following:--\n\n(1) A ball is drawn from a bag containing nine black\nballs and one white: what is the chance of its being the\nwhite ball?\n\n(2) A ball is drawn from a bag containing ten balls, and\nis found to be white; what is the chance of there having\nbeen but that one white ball in the bag?\n\nThe class of which the first example is a simple instance\nhas been already abundantly discussed. The interpretation\nof it is as follows: If balls be continually drawn and replaced,\nthe proportion of white ones to the whole number\ndrawn will tend towards the fraction 1/10. The contemplated\naction is a single one, but we view it as one of the above\nseries; at least our opinion is formed upon that assumption.\nWe conclude that we are going to take one of a series of\nevents which may appear individually fortuitous, but in\nwhich, in the long run, those of a given kind are one-tenth of\nthe whole; this kind (white) is then singled out by anticipation.\nBy stating that its chance is 1/10, we merely mean to\nassert this physical fact, together with such other mental\nfacts, emotions, inferences, &c., as may be properly associated\nwith it.\n\n11. Have we to interpret the second example in a\ndifferent way? Here also we have a single instance, but the\nnature of the question would seem to decide that the only\nseries to which it can properly be referred is the following:--Balls\nare continually drawn from _different_ bags each containing\nten, and are always found to be white; what is ultimately\nthe proportion of cases in which they will be found to have\nbeen taken from bags with only one white ball in them?\nNow it may be readily shown[5] that time has nothing to\ndo with the question; omitting therefore the consideration\nof this element, we have for the two series from which our\nopinions in these two examples respectively are to be\nformed:--(1) balls of different colours presented to us in a\ngiven ultimate ratio; (2) bags with different contents similarly\npresented. From these data respectively we have to\nassign their due weight to our anticipations of (1) a white\nball; (2) a bag containing but one white ball. So stated the\nproblems would appear to be formally identical.\n\nWhen, however, we begin the practical work of solving\nthem we perceive a most important distinction. In the first\nexample there is not much that is arbitrary; balls would\nunder such circumstance really come out more or less accurately\nin the proportion expected. Moreover, in case it\nshould be objected that it is difficult to prove that they will\ndo so, it does not seem an unfair demand to say that the balls\nare to be 'well-mixed' or 'fairly distributed,' or to introduce\nany of the other conditions by which, under the semblance of\njudging _\u00e0 priori_, we take care to secure our prospect of a\nseries of the desired kind. But we cannot say the same in\nthe case of the second example.\n\n12. The line of proof by which it is generally attempted\nto solve the second example is of this kind;--It is\nshown that there being one white ball for certain in the bag,\nthe only possible antecedents are of ten kinds, viz. bags,\neach of which contains ten balls, but in which the white\nballs range respectively from one to ten in number. This of\ncourse imposes limits upon the kind of terms to be found\nin our series. But we want more than such limitations, we\nmust know the proportions in which these terms are ultimately\nfound to arrange themselves in the series. Now this\nrequires an experience about bags which may not, and indeed\nin a large proportion of similar cases, cannot, be given\nto us. If therefore we are to solve the question at all we\nmust make an assumption; let us make the following;--_that\neach of the bags described above occurs equally often_,--and see\nwhat follows. The bags being drawn from equally often, it\ndoes not follow that they will each yield equal numbers of\nwhite balls. On the contrary they will, as in the last\nexample, yield them in direct proportion to the number of\nsuch balls which they contain. The bag with one white\nand nine black will yield a white ball once in ten times; that\nwith two white, twice; and so on. The result of this, it will\nbe easily seen, is that in 100 drawings there will be obtained\non the average 55 white balls and 45 black. Now with\nthose drawings that do not yield white balls we have, by the\nquestion, nothing to do, for that question postulated the\ndrawing of a white ball as an accomplished fact. The series\nwe want is therefore composed of those which do yield white.\nNow what is the additional attribute which is found in some\nmembers, and in some members only, of this series, and\nwhich we mentally anticipate? Clearly it is the attribute of\nhaving been drawn from a bag which only contained one of\nthese white balls. Of these there is, out of the 55 drawings,\nbut one. Accordingly the required chance is 1/55. That is to\nsay, the white ball will have been drawn from the bag containing\nonly that one white, once in 55 times.\n\n13. Now, with the exception of the passage in italics,\nthe process here is precisely the same as in the other example;\nit is somewhat longer only because we are not able to\nappeal immediately to experience, but are forced to try to\ndeduce what the result will be, though the validity of this\ndeduction itself rests, of course, ultimately upon experience.\nBut the above passage is a very important one. It is scarcely\nnecessary to point out how arbitrary it is.\n\nFor _is_ the supposition, that the different specified kinds\nof bags are equally likely, the most reasonable supposition\nunder the circumstances in question? One man may think\nit is, another may take a contrary view. In fact in an excellent\nmanual[6] upon the subject a totally different supposition\nis made, at any rate in one example; it is taken for granted\nin that instance, not that every possible number of black and\nwhite balls respectively is equally likely, but that every\npossible way of getting each number is equally likely, whence\nit follows that bags with an intermediate number of black\nand white balls are far more likely than those with an extreme\nnumber of either. On this supposition five black\nand five white being obtainable in 252 ways against the\nten ways of obtaining one white and nine black, it follows\nthat the chance that we have drawn from a bag of\nthe latter description is much less than on the hypothesis\nfirst made. The chance, in fact, becomes now 1/512 instead\nof 1/55. In the one case each distinct result is considered\nequally likely, in the other every distinct way of getting\neach result.\n\n14. Uncertainties of this kind are peculiarly likely to\narise in these inverse probabilities, because when we are\nmerely given an effect and told to look out for the chance of\nsome assigned cause, we are often given no clue as to the relative\nprevalence of these causes, but are left to determine them\non general principles. Give us either their actual prevalence\nin statistics, or the conditions by which such prevalence is\nbrought about, and we know what to do; but without the\nhelp of such data we are reduced to guessing. In the above\nexample, if we had been told how the bag had been originally\nfilled, that is by what process, or under what circumstances,\nwe should have known what to do. If it had been filled at\nrandom from a box containing equal numbers of black and\nwhite balls, the supposition in Mr Whitworth's example is\nthe most reasonable; but in the absence of any such information\nas this we are entirely in the dark, and the supposition\nmade in \u00a712 is neither more nor less trustworthy and\nreasonable than many others, though it doubtless possesses\nthe merit of superior simplicity.[7] If the reader will recur to\nCh. V. \u00a7\u00a74, 5, he will find this particular difficulty fully\nexplained. Everybody practically admits that a certain\ncharacteristic arrangement or distribution has to be introduced\nat some prior stage; and that, as soon as this stage\nhas been selected, there are no further theoretic difficulties\nto be encountered. But when we come to decide, in examples\nof the class in question, at what stage it is most reasonable\nto make our postulate, we are often left without any very\ndefinite or rational guidance.\n\n15. When, however, we take what may be called, by\ncomparison with the above purely artificial examples, instances\npresented by nature, much of this uncertainty will disappear,\nand then all real distinction between direct and inverse\nprobability will often vanish. In such cases the causes are\nmostly determined by tolerably definite rules, instead of\nbeing a mere cloud-land of capricious guesses. We may\neither find their relative frequency of occurrence by reference\nto tables, or may be able to infer it by examination of\nthe circumstances under which they are brought about.\nAlmost any simple example would then serve to illustrate\nthe fact that under such circumstances the distinction\nbetween direct and inverse probability disappears altogether,\nor merely resolves itself into one of _time_, which, as will be\nmore fully shown in a future chapter, is entirely foreign to\nour subject.\n\nIt is not of course intended to imply that difficulties\nsimilar to those mentioned above do not occasionally invade\nus here also. As already mentioned, they are, if not inherent\nin the subject, at any rate almost unavoidable in comparison\nwith the simpler and more direct procedure of determining\nwhat is likely to follow from assigned conditions. What is\nmeant is that so long as we confine ourselves within the\ncomparatively regular and uniform field of natural sequences\nand co-existences, statistics of causes may be just as readily\navailable as those of effects. There will not be much more\nthat is arbitrary in the one than in the other. But of course\nthis security is lost when, as will be almost immediately\nnoticed, what may be called metaphysical rather than natural\ncauses are introduced into the enquiry.\n\nFor instance, it is known that in London about 20 people\ndie per thousand each year. Suppose it also known that of\nevery 100 deaths there are about 4 attributable to bronchitis.\nThe odds therefore against any unknown person dying of\nbronchitis in a given year are 1249 to 1. Exactly the same\nstatistics are available to solve the inverse problem:--A man\nis dead, what is the chance that he died of bronchitis? Here,\nsince the man's death is taken for granted, we do not require\nto know the general average mortality. All that we want is\nthe proportional mortality from the disease in question as\ngiven above. If Probability dealt only with inferences\nfounded in this way upon actual statistics, and these tolerably\nextensive, it is scarcely likely that any distinction such\nas this between direct and inverse problems would ever have\nbeen drawn.\n\n16. Considered therefore as a contribution to the theory\nof the subject, the distinction between Direct and Inverse Probability\nmust be abandoned. When the appropriate statistics\nare at hand the two classes of problems become identical\nin method of treatment, and when they are not we have no\nmore right to extract a solution in one case than in the other.\nThe discussion however may serve to direct renewed attention\nto another and far more important distinction. It will\nremind us that there is one class of examples to which the\ncalculus of Probability is rightfully applied, because statistical\ndata are all we have to judge by; whereas there are other\nexamples in regard to which, if we will insist upon making\nuse of these rules, we may either be deliberately abandoning\nthe opportunity of getting far more trustworthy information\nby other means, or we may be obtaining solutions about\nmatters on which the human intellect has no right to any\ndefinite quantitative opinion.\n\n17. The nearest approach to any practical justification\nof such judgments that I remember to have seen is afforded\nby cases of which the following example is a specimen:--\n\"Of 10 cases treated by Lister's method, 7 did well and 3 suffered\nfrom blood-poisoning: of 14 treated with ordinary\ndressings, 9 did well and 5 had blood-poisoning; what are\nthe odds that the success of Lister's method was due to\nchance?\".[8] Or, to put it into other words, a short experience\nhas shown an actual superiority in one method over the\nother: what are the chances that an indefinitely long experience,\nunder similar conditions, will confirm this superiority?\n\nThe proposer treated this as a 'bag and balls' problem,\nanalogous to the following: 10 balls from one bag gave\n7 white and 3 black, 14 from another bag gave 9 white and\n5 black: what is the chance that the actual ratio of white to\nblack balls was greater in the former than in the latter?--this\nactual ratio being of course considered a true indication\nof what would be the ultimate proportions of white and black\ndrawings. This seems to me to be the only reasonable way\nof treating the problem, if it is to be considered capable of\nnumerical solution at all.\n\nOf course the inevitable assumption has to be made here\nabout the equal prevalence of the different possible kinds of\nbag,--or, as the supporters of the justice of the calculation\nwould put it, of the obligation to assume the equal _\u00e0 priori_\nlikelihood of each kind,--but I think that in this particular\nexample the arbitrariness of the assumption is less than\nusual. This is because the problem discusses simply a\nbalance between two extremely similar cases, and there is a\ncertain set-off against each other of the objectionable assumptions\non each side. Had _one_ set of experiments only been\nproposed, and had we been asked to evaluate the probability\nof continued repetition of them confirming their verdict, I\nshould have felt all the scruples I have already mentioned.\nBut here we have got two sets of experiments carried on\nunder almost exactly similar circumstances, and there is\ntherefore less arbitrariness in assuming that their unknown\nconditions are tolerably equally prevalent.\n\n18. Examples of the description commonly introduced\nseem objectionable enough, but if we wish to realize to its\nfull extent the vagueness of some of the problems submitted\nto this Inverse Probability, we have not far to seek. In\nnatural as in artificial examples, where statistics are unattainable\nthe enquiry becomes utterly hopeless, and all attempts\nat laying down rules for calculation must be abandoned.\nTake, for instance, the question which has given rise to some\ndiscussion,[9] whether such and such groups of stars are or are\nnot to be regarded as the results of an accidental distribution;\nor the still wider and vaguer question, whether such and\nsuch things, or say the world itself, have been produced by\nchance?\n\nIn cases of this kind the insuperable difficulty is in determining\nwhat sense exactly is to be attached to the words\n'accidental' and 'random' which enter into the discussion.\nSome account was given, in the fourth chapter, of their\nscientific and conventional meaning in Probability. There\nseem to be the same objections to generalizing them out of\nsuch relation, as there is in metaphysics to talking of the\nInfinite or the Absolute. Infinite magnitude, or infinite\npower, one can to some extent comprehend, or at least one\nmay understand what is being talked about, but '_the_ infinite'\nseems to me a term devoid of meaning. So of anything\nsupposed to have been produced at random: tell us the\nnature of the agency, the limits of its randomness and so on,\nand we can venture upon the problem, but without such data\nwe know not what to do. The further consideration of such\na problem might, I think, without arrogance be relegated to\nthe Chapter on Fallacies. Accordingly any further remarks\nwhich I have to make upon the subject will be found there,\nand at the conclusion of the chapter on Causation and\nDesign.\n\n\n1. It might be more accurate to speak of 'incompatible hypotheses with\n  respect to any individual case', or 'mutually exclusive classes of\n  events'.\n\n2. The examples, of this kind, referring to human mortality are taken\n  from the Carlisle tables. These differ considerably, as is well\n  known, from other tables, but we have the high authority of De\n  Morgan for regarding them as the best representative of the average\n  mortality of the English middle classes at the present day.\n\n3. I say, _almost_ any proportion, because, as may easily be seen,\n  arithmetic imposes certain restrictions upon the assumptions that\n  can be made. We could not, for instance, suppose that all the\n  black-haired men are short-sighted, for in any given batch of men\n  the former are more numerous. But the range of these restrictions is\n  limited, and their existence is not of importance in the above\n  discussion.\n\n4. _Essay on Probabilities_, p. 53. I have been reminded that in his\n  article on Probability in the _Encyclop\u00e6dia Metropolitana_ he has\n  stated that such rules involve no new principle.\n\n5. This point will be fully discussed in a future chapter, after the\n  general stand-point of an objective system of logic has been\n  explained and illustrated.\n\n6. Whitworth's _Choice and Chance_, Ed. II., p. 123. See also Boole's\n  _Laws of Thought_, p. 370.\n\n7. Opinions differ about the defence of such suppositions, as they do\n  about the nature of them. Some writers, admitting the above\n  assumption to be doubtful, call it the most impartial\n  hypothesis. Others regard it as a sort of mean hypothesis.\n\n8. _Educational Times_; Reprint, Vol. xxxvii. p. 40. The question was\n  proposed by Dr. Macalister and gave rise to considerable controversy.\n  As usual with problems of this inverse kind hardly any two of the\n  writers were in agreement as to the assumptions to be made, or\n  therefore as to the numerical estimate of the odds.\n\n9. See Todhunter's _History_, pp. 333, 4.\n\n  There is an interesting discussion upon this question by the late\n  J. D. Forbes in a paper in the _Philosophical Magazine_ for\n  Dec. 1850. It was replied to in a subsequent number by Prof. Donkin.\n\n\n\n\nCHAPTER VIII.\n\n\n_THE RULE OF SUCCESSION._[1]\n\n1. A word of apology may be offered here for the introduction of a new\n  name. The only other alternative would have been to entitle the rule\n  one of _Induction_. But such a title I cannot admit, for reasons\n  which will be almost immediately explained.\n\n\n1. In the last chapter we discussed at some length the\nnature of the kinds of inference in Probability which correspond\nto those termed, in Logic, immediate and mediate inferences.\nWe ascertained what was the meaning of saying, for\nexample, that the chance of any given man A. B. dying\nin a year is 1/3, when concluded from the general proposition\nthat one man out of three in his circumstances dies. We\nalso discussed the nature and evidence of rules of a more\ncompletely inferential character. But to stop at this point\nwould be to take a very imperfect view of the subject. If\nProbability is a science of real inference about things, it\nmust surely lead up to something more than such merely\nformal conclusions; we must be able, if not by means of it, at\nany rate by some means, to step beyond the limits of what\nhas been actually observed, and to draw conclusions about\nwhat is as yet unobserved. This leads at once to the question,\nWhat is the connection of Probability with Induction?\nThis is a question into which it will be necessary to enter\nnow with some minuteness.\n\nThat there is a close connection between Probability and\nInduction, must have been observed by almost every one\nwho has treated of either subject; I have not however seen\nany account of this connection that seemed to me to be\nsatisfactory. An explicit description of it should rather be\nsought in treatises upon the narrower subject, Probability;\nbut it is precisely here that the most confusion is to be\nfound. The province of Probability being somewhat narrow,\nincursions have been constantly made from it into the adjacent\nterritory of Induction. In this way, amongst the\narithmetical rules discussed in the last chapter, others have\nbeen frequently introduced which ought not in strictness to\nbe classed with them, as they rest on an entirely different\nbasis.\n\n2. The origin of such confusion is easy of explanation;\nit arises, doubtless, from the habit of laying undue\nstress upon the _subjective_ side of Probability, upon that\nwhich treats of the quantity of our belief upon different\nsubjects and the variations of which that quantity is susceptible.\nIt has been already urged that this variation of\nbelief is at most but a constant accompaniment of what is\nreally essential to Probability, and is moreover common to\nother subjects as well. By defining the science therefore\nfrom this side these other subjects would claim admittance\ninto it; some of these, as Induction, have been accepted, but\nothers have been somewhat arbitrarily rejected. Our belief\nin a wider proposition gained by Induction is, prior to verification,\nnot so strong as that of the narrower generalization\nfrom which it is inferred. This being observed, a so-called\nrule of probability has been given by which it is supposed\nthat this diminution of assent could in many instances be\ncalculated.\n\nBut _time_ also works changes in our conviction; our belief\nin the happening of almost every event, if we recur to it long\nafterwards, when the evidence has faded from the mind, is\nless strong than it was at the time. Why are not rules of\noblivion inserted in treatises upon Probability? If a man is\ntold how firmly he ought to expect the tide to rise again,\nbecause it has already risen ten times, might he not also ask\nfor a rule which should tell him how firm should be his belief\nof an event which rests upon a ten years' recollection?[1] The\ninfractions of a rule of this latter kind could scarcely be more\nnumerous and extensive, as we shall see presently, than those\nof the former confessedly are. The fact is that the agencies,\nby which the strength of our conviction is modified, are so\nindefinitely numerous that they cannot all be assembled into\none science; for purposes of definition therefore the quantity\nof belief had better be omitted from consideration, or at any\nrate regarded as a mere appendage, and the science, defined\nfrom the other or statistical side of the subject, in which,\nas has been shown, a tolerably clear boundary-line can be\ntraced.\n\n3. Induction, however, from its importance does merit\na separate discussion; a single example will show its bearing\nupon this part of our subject. We are considering the prospect\nof a given man, A. B. living another year, and we find\nthat nine out of ten men of his age do survive. In forming\nan opinion about his surviving, however, we shall find that\nthere are in reality two very distinct causes which aid in\ndetermining the strength of our conviction; distinct, but in\npractice so intimately connected that we are very apt to\noverlook one, and attribute the effect entirely to the other.\n\n(I.) There is that which strictly belongs to Probability;\nthat which (as was explained in Chap VI.) measures our\nbelief of the individual case as deduced from the general\nproposition. Granted that nine men out of ten of the kind\nto which A. B. belongs do live another year, it obviously\ndoes not follow at all necessarily that _he_ will. We describe\nthis state of things by saying, that our belief of his surviving\nis diminished from certainty in the ratio of 10 to 9, or, in\nother words, is measured by the fraction 9/10.\n\n(II.) But are we certain that nine men out of ten like\nhim _will_ live another year? we know that they have so survived\nin time past, but will they continue to do so? Since\nA. B. is still alive it is plain that this proposition is to a\ncertain extent assumed, or rather obtained by Induction.\nWe cannot however be as certain of the inductive inference\nas we are of the data from which it was inferred. Here,\ntherefore, is a second cause which tends to diminish our\nbelief; in practice these two causes always accompany each\nother, but in thought they can be separated.\n\nThe two distinct causes described above are very liable\nto be confused together, and the class of cases from which\nexamples are necessarily for the most part drawn increases\nthis liability. The step from the statement 'all men have\ndied in a certain proportion' to the inference 'they will continue\nto die in that proportion' is so slight a step that it is\nunnoticed, and the diminution of conviction that should\naccompany it is unsuspected. In what are called _\u00e0 priori_\nexamples the step is still slighter. We feel so certain about\nthe permanence of the laws of mechanics, that few people\nwould think of regarding it as an inference when they\nbelieve that a die will in the long run turn up all its faces\nequally often, because other dice have done so in time\npast.\n\n4. It has been already pointed out (in Chapter VI.)\nthat, so far as concerns that definition of Probability which\nregards it as the science which discusses the degree and\nmodifications of our belief, the question at issue seems to be\nsimply this:--Are the causes alluded to above in (II.) capable\nof being reduced to one simple coherent scheme, so that any\nuniversal rules for the modification of assent can be obtained\nfrom them? If they are, strong grounds will have been\nshown for classing them with (I.), in other words, for considering\nthem as rules of probability. Even then they\nwould be rules practically of a very different kind, contingent\ninstead of necessary (if one may use these terms without\ncommitting oneself to any philosophical system), but this\nobjection might perhaps be overruled by the greater simplicity\nsecured by classing them together. This view is, with\nvarious modifications, generally adopted by writers on Probability,\nor at least, as I understand the matter, implied by\ntheir methods of definition and treatment. Or, on the other\nhand, must these causes be regarded as a vast system, one\nmight almost say a chaos, of perfectly distinct agencies;\nwhich may indeed be classified and arranged to some extent,\nbut from which we can never hope to obtain any rules of\nperfect generality which shall not be subject to constant\nexception? If so, but one course is left; to exclude them\nall alike from Probability. In other words, we must assume\nthe general proposition, viz. that which has been described\nthroughout as our starting-point, to be given to us; it may\nbe obtained by any of the numerous rules furnished by\nInduction, or it may be inferred deductively, or given by our\nown observation; its value may be diminished by its depending\nupon the testimony of witnesses, or its being recalled by\nour own memory. Its real value may be influenced by\nthese causes or any combinations of them; but all these are\npreliminary questions with which we have nothing directly\nto do. We assume our statistical proposition to be true,\nneglecting the diminution of its value by the process of\nattainment; we take it up first at this point and then apply\nour rules to it. We receive it in fact, if one may use the\nexpression, _ready-made_, and ask no questions about the process\nor completeness of its manufacture.\n\n5. It is not to be supposed, of course, that any writers\nhave seriously attempted to reduce to one system of calculation\nall the causes mentioned above, and to embrace in one\nformula the diminution of certainty to which the inclusion of\nthem subjects us. But on the other hand, they have been\nunwilling to restrain themselves from all appeal to them.\nFrom an early period in the study of the science attempts\nhave been made to proceed, by the Calculus of Probability,\nfrom the observed cases to adjacent and similar cases. In\npractice, as has been already said, it is not possible to avoid\nsome extension of this kind. But it should be observed,\nthat in these instances the divergence from the strict ground\nof experience is not in reality recognized, at least not as a\npart of our logical procedure. We have, it is true, wandered\nsomewhat beyond it, and so obtained a wider proposition\nthan our data strictly necessitated, and therefore one of less\ncertainty. Still we assume the conclusion given by induction\nto be equally certain with the data, or rather omit all\nnotice of the divergence from consideration. It is assumed\nthat the unexamined instances will resemble the examined,\nan assumption for which abundant warrant may exist; the\ntheory of the calculation rests upon the supposition that\nthere will be no difference between them, and the practical\nerror is insignificant simply because this difference is small.\n\n6. But the rule we are now about to discuss, and\nwhich may be called the Rule of Succession, is of a very\ndifferent kind. It not only recognizes the fact that we are\nleaving the ground of past experience, but takes the consequences\nof this divergence as the express subject of its calculation.\nIt professes to give a general rule for the measure of\nexpectation that we should have of the reappearance of a\nphenomenon that has been already observed any number of\ntimes. This rule is generally stated somewhat as follows:\n\"To find the chance of the recurrence of an event already\nobserved, divide the number of times the event has been\nobserved, increased by one, by the same number increased\nby two.\"\n\n7. It will be instructive to point out the origin of\nthis rule; if only to remind the reader of the necessity of\nkeeping mathematical formul\u00e6 to their proper province,\nand to show what astonishing conclusions are apt to\nbe accepted on the supposed warrant of mathematics.\nRevert then to the example of Inverse Probability on p. 182.\nWe saw that under certain assumptions, it would\nfollow that when a single white ball had been drawn\nfrom a bag known to contain 10 balls which were white\nor black, the chance could be determined that there was\nonly one white ball in it. Having done this we readily\ncalculate 'directly' the chance that this white ball will\nbe drawn next time. Similarly we can reckon the chances\nof there being two, three, &c. up to ten white balls in it,\nand determine on each of these suppositions the chance\nof a white ball being drawn next time. Adding these\ntogether we have the answer to the question:--a white\nball has been drawn once from a bag known to contain\nten balls, white or black; what is the chance of a second\ntime drawing a white ball?\n\nSo far only arithmetic is required. For the next step we\nneed higher mathematics, and by its aid we solve this\nproblem:--A white ball has been drawn m times from a\nbag which contains any number, we know not what, of\nballs each of which is white or black, find the chance of\nthe next drawing also yielding a white ball. The answer is\n(m + 1)/(m + 2).\n\nThus far mathematics. Then comes in the physical\nassumption that the universe may be likened to such a bag\nas the above, in the sense that the above rule may be\napplied to solve this question:--an event has been observed\nto happen m times in a certain way, find the chance that\nit will happen in that way next time. Laplace, for instance,\nhas pointed out that at the date of the writing of his _Essai\nPhilosophique_, the odds in favour of the sun's rising again\n(on the old assumption as to the age of the world) were\n1,826,214 to 1. De Morgan says that a man who standing\non the bank of a river has seen ten ships pass by with flags\nshould judge it to be 11 to 1 that the next ship will also\ncarry a flag.\n\n8. It is hard to take such a rule as this seriously, for\nthere does not seem to be even that moderate confirmation\nof it which we shall find to hold good in the case of the\napplication of abstract formul\u00e6 to the estimation of the\nevidence of witnesses. If however its validity is to be discussed\nthere appear to be two very distinct lines of enquiry\nalong which we may be led.\n\n(1) In the first place we may take it for what it professes\nto be, and for what it is commonly understood to\nbe, viz. a rule which assigns the measure of expectation\nwe ought to entertain of the recurrence of the event under\nthe circumstances in question. Of course, on the view\nadopted in this work, we insist on enquiring whether it is\nreally true that on the average events do thus repeat their\nperformance in accordance with this law. Thus tested, no\none surely would attempt to defend such a formula. So\nfar from past occurrence being a ground for belief in future\nrecurrence, there are (as will be more fully pointed out\nin the Chapter on Fallacies) plenty of cases in which the\ndirect contrary holds good. Then again a rule of this kind\nis subject to the very serious perplexity to be explained\nin our next chapter, arising out of the necessary arbitrariness\nof such inverse reference. That is, when an event has\nhappened but a few times, we have no certain guide; and\nwhen it has happened but once,[2] we have no guide whatever,\nas to the class of cases to which it is to be referred. In\nthe example above, about the flags, why did we stop short at\nthis notion simply, instead of specifying the size, shape, &c.\nof the flags?\n\nDe Morgan, it must be remembered, only accepts this rule\nin a qualified sense. He regards it as furnishing a\n_minimum_ value for the amount of our expectation. He\nterms it \"the rule of probability of a _pure induction_,\" and\nsays of it, \"The probabilities shown by the above rules\nare merely _minima_ which may be augmented by other\nsources of knowledge.\" That is, he recognizes only those\ninstances in which our belief in the Uniformity of Nature\nand in the existence of special laws of causation comes in\nto supplement that which arises from the mere frequency\nof past occurrence. This however does not meet those cases\nin which past occurrence is a positive ground of disbelief in\nfuture recurrence.\n\n9. (2) There is however another and very different\nview which might be taken of such a rule. It is one, an\nobscure recognition of which has very likely had much to\ndo with the acceptance which the rule has received.\n\nWhat we might suppose ourselves to be thus expressing\nis,--not the measure of rational expectation which might be\nheld by minds sufficiently advanced to be able to classify\nand to draw conscious inferences, but,--the law according to\nwhich the primitive elements of belief were started and\ndeveloped. Of course such an interpretation as this would\nbe equivalent to quitting the province of Logic altogether\nand crossing over into that of Psychology; but it would be a\nperfectly valid line of enquiry. We should be attempting\nnothing more than a development of the researches of\nFechner and his followers in psychophysical measurement.\nOnly then we ought, like them, not to start with any analogy\nof a ballot box and its contents, but to base our enquiry\non careful determination of the actual mental phenomena\nexperienced. We know how the law has been determined\nin accordance with which the intensity of the feeling of\n_light_ varies with that of its objective source. We see how it\nis possible to measure the growth of _memory_ according to\nthe number of repetitions of a sentence or a succession\nof mere syllables. In this latter case, for instance, we just\ntry experiments, and determine how much better a man can\nremember any utterances after eight hearings than after\nseven.[3]\n\nNow this case furnishes a very close parallel to our\nsupposed attempt to measure the increase of intensity of\nbelief after repeated recurrence. That is, if it were possible\nto experiment in this order of mental phenomena, we ought\nsimply to repeat a phenomenon a certain number of times\nand then ascertain by actual introspection or by some simple\ntest, how fast the belief was increasing. Thus viewed the\nproblem seems to me a hopeless one. The difficulties are\nserious enough, when we are trying to measure our simple\nsensations, of laying aside the effects of past training, and of\nattempting, as it were, to leave the mind open and passive\nto mere reception of stimuli. But if we were to attempt\nin this way to measure our belief these difficulties would\nbecome quite insuperable. We can no more divest ourselves\nof past training here than we can of intelligence or\nthought. I do not see how any one could possibly avoid\nclassing the observed recurrences with others which he had\nexperienced, and of being thus guided by special analogies\nand inductions instead of trusting solely to De Morgan's\n'pure induction'. The same considerations tend to rebut\nanother form of defence for the rule in question. It is\nurged, for instance, that we may at least resort to it in\nthose cases in which we are in entire ignorance as to the\nnumber and nature of the antecedents. This is a position to\nwhich I can hardly conceive it possible that we should ever\nbe reduced. However remote or exceptional may be the\nphenomenon selected we may yet bring it into relation with\nsome accepted generalizations and thus draw our conclusions\nfrom these rather than from purely _\u00e0 priori_ considerations.\n\n10. Since then past acquisitions cannot be laid aside\nor allowed for, the only remaining resource would be to\nexperiment upon the infant mind. One would not like\nto pronounce that any line of enquiry is impossible; but\nthe difficulties would certainly be enormous. And interesting\nas the facts would be, supposing that we had succeeded\nin securing them, they would not be of the slightest importance\nin Logic. However the question were settled:--whether,\nfor instance, we proved that the sentiment or\nemotion of belief grew up slowly and gradually from a sort\nof zero point under the impress of repetition of experience;\nor whether we proved that a single occurrence produced\ncomplete belief in the repetition of the event, so that\nexperience gradually untaught us and weakened our convictions;--in\nno case would the mature mind gain any aid\nas to what it ought to believe.\n\nI cannot but think that some such view as this must\noccasionally underlie the acceptance which this rule has received.\nFor instance, Laplace, though unhesitatingly adopting\nit as a real, that is, objective rule of inference, has gone\ninto so much physiological and psychological matter towards\nthe end of his discussion (_Essai philosophique_) as to suggest\nthat what he had in view was the natural history of belief\nrather than its subsequent justification.\n\nAgain, the curious doctrine adopted by Jevons, that the\nprinciples of Induction rest entirely upon the theory of\nProbability,--a very different doctrine from that which is\nconveyed by saying that all knowledge of facts is _probable_\nonly, i.e. not necessary,--seems unintelligible except on some\nsuch interpretation. We shall have more to say on this\nsubject in our next chapter. It will be enough here to\nremark that in our present reflective and rational stage\nwe find that every inference in Probability involves some\nappeal to, or support from, Induction, but that it is impossible\nto base either upon the other. However far back\nwe try to push our way, and however disposed we might be\nto account for our ultimate beliefs by Association, it seems\nto me that so long as we consider ourselves to be dealing\nwith rules of inference we must still distinguish between\nInduction and Probability.\n\n\n1. John Craig, in his often named work, _Theologi\u00e6 Christian\u00e6\n  Principia Mathematica_ (Lond. 1699) attempted something in this\n  direction when he proposed to solve such problems as:--Quando\n  evanescet probabilitas cujusvis Histori\u00e6, cujus subjectum est\n  transiens, viv\u00e2 tantum voce transmiss\u00e6, determinare.\n\n2. When m = 1 the fraction becomes 2/3; i.e. the odds are 2 to 1 in\n  favour of recurrence. And there are writers who accept this\n  result. For instance, Jevons (_Principles of Science_ p. 258) says\n  \"Thus on the first occasion on which a person sees a shark, and\n  notices that it is accompanied by a little pilot fish, the odds are\n  2 to 1 that the next shark will be so accompanied.\"  To say nothing\n  of the fact that recognizing and naming the fish implies that they\n  have often been seen before, how many of the observed\n  characteristics of that single 'event' are to be considered\n  essential?  Must the pilot precede; and at the same distance? Must\n  we consider the latitude, the ocean, the season, the species of\n  shark, as matter also of repetition on the next occasion?  and so\n  on. I cannot see how the Inductive problem can be even intelligibly\n  stated, for quantitative purposes, on the first occurrence of any\n  event.\n\n3. See in _Mind_ (x. 454) Mr Jacob's account of the researches of Herr\n  Ebbinghaus as described in his work _Ueber das Ged\u00e4chtniss_.\n\n\n\n\nCHAPTER IX.\n\n\n_INDUCTION AND ITS CONNECTION WITH PROBABILITY._\n\n1. We were occupied, during the last chapter, with the\nexamination of a rule, the object of which was to enable\nus to make inferences about instances as yet unexamined.\nIt was professedly, therefore, a rule of an inductive character.\nBut, in the form in which it is commonly expressed,\nit was found to fail utterly. It is reasonable therefore to\nenquire at this point whether Probability is entirely a formal\nor deductive science, or whether, on the other hand, we are\nable, by means of it, to make valid inferences about instances\nas yet unexamined. This question has been already in part\nanswered by implication in the course of the last two chapters.\nIt is proposed in the present chapter to devote a fuller\ninvestigation to this subject, and to describe, as minutely as\nlimits will allow, the nature of the connection between Probability\nand Induction. We shall find it advisable for clearness\nof conception to commence our enquiry at a somewhat\nearly stage. We will travel over the ground, however, as\nrapidly as possible, until we approach the boundary of what\ncan properly be termed Probability.\n\n2. Let us then conceive some one setting to work to\ninvestigate nature, under its broadest aspect, with the view\nof systematizing the facts of experience that are known, and\nthence (in case he should find that this is possible) discovering\nothers which are at present unknown. He observes a\nmultitude of phenomena, physical and mental, contemporary\nand successive. He enquires what connections are there\nbetween them? what rules can be found, so that some of\nthese things being observed I can infer others from them?\nWe suppose him, let it be observed, deliberately resolving to\ninvestigate the things themselves, and not to be turned\naside by any prior enquiry as to there being laws under\nwhich the mind is compelled to judge of the things. This\nmay arise either from a disbelief in the existence of any\nindependent and necessary mental laws, and a consequent\nconviction that the mind is perfectly competent to observe\nand believe anything that experience offers, and should\nbelieve nothing else, or simply from a preference for investigations\nof the latter kind. In other words, we suppose him\nto reject Formal Logic, and to apply himself to a study of\nobjective existences.\n\nIt must not for a moment be supposed that we are here\ndoing more than conceiving a fictitious case for the purpose\nof more vividly setting before the reader the nature of the\ninductive process, the assumptions it has to make, and the\ncharacter of the materials to which it is applied. It is not\npsychologically possible that any one should come to the study\nof nature with all his mental faculties in full perfection, but\nvoid of all materials of knowledge, and free from any bias as\nto the uniformities which might be found to prevail around\nhim. In practice, of course, the form and the matter--the\nlaws of belief or association, and the objects to which they\nare applied--act and react upon one another, and neither\ncan exist in any but a low degree without presupposing the\nexistence of the other. But the supposition is perfectly legitimate\nfor the purpose of calling attention to the requirements\nof such a system of Logic, and is indeed nothing more\nthan what has to be done at almost every step in psychological\nenquiry.[1]\n\n3. His task at first might be conceived to be a slow\nand tedious one. It would consist of a gradual accumulation\nof individual instances, as marked out from one another\nby various points of distinction, and connected with one\nanother by points of resemblance. These would have to be\nrespectively distinguished and associated in the mind, and\nthe consequent results would then be summed up in general\npropositions, from which inferences could afterwards be\ndrawn. These inferences could, of course, contain no new\nfacts, they would only be repetitions of what he or others\nhad previously observed. All that we should have so far\ndone would have been to make our classifications of things\nand then to appeal to them again. We should therefore be\nkeeping well within the province of ordinary logic, the processes\nof which (whatever their ultimate explanation) may\nof course always be expressed, in accordance with Aristotle's\nDictum, as ways of determining whether or not we can show\nthat one given class is included wholly or partly within\nanother, or excluded from it, as the case may be.\n\n4. But a very short course of observation would suggest\nthe possibility of a wide extension of his information.\nExperience itself would soon detect that events were connected\ntogether in a regular way; he would ascertain that\nthere are 'laws of nature.' Coming with no _\u00e0 priori_ necessity\nof believing in them, he would soon find that as a matter\nof fact they do exist, though he could not feel any certainty\nas to the extent of their prevalence. The discovery of this\narrangement in nature would at once alter the plan of his proceedings,\nand set the tone to the whole range of his methods\nof investigation. His main work now would be to find out\nby what means he could best discover these laws of nature.\n\nAn illustration may assist. Suppose I were engaged in\nbreaking up a vast piece of rock, say slate, into small pieces.\nI should begin by wearily working through it inch by inch.\nBut I should soon find the process completely changed owing\nto the existence of _cleavage_. By this arrangement of things\na very few blows would do the work--not, as I might possibly\nhave at first supposed, to the extent of a few inches--but\nright through the whole mass. In other words, by the\nprocess itself of cutting, as shown in experience, and by\nnothing else, a constitution would be detected in the things\nthat would make that process vastly more easy and extensive.\nSuch a discovery would of course change our tactics.\nOur principal object would thenceforth be to ascertain the\nextent and direction of this cleavage.\n\nSomething resembling this is found in Induction. The\ndiscovery of laws of nature enables the mind to dart with its\ninferences from a few facts completely through a whole class\nof objects, and thus to acquire results the successive individual\nattainment of which would have involved long and\nwearisome investigation, and would indeed in multitudes\nof instances have been out of the question. We have no\ndemonstrative proof that this state of things is universal;\nbut having found it prevail extensively, we go on with the\nresolution at least to try for it everywhere else, and we are\nnot disappointed. From propositions obtained in this way,\nor rather from the original facts on which these propositions\nrest, we can make _new_ inferences, not indeed with absolute\ncertainty, but with a degree of conviction that is of the\nutmost practical use. We have gained the great step of\nbeing able to make trustworthy generalizations. We conclude,\nfor instance, not merely that John and Henry die,\nbut that all men die.\n\n5. The above brief investigation contains, it is hoped,\na tolerably correct outline of the nature of the Inductive\ninference, as it presents itself in Material or Scientific Logic.\nIt involves the distinction drawn by Mill, and with which\nthe reader of his _System of Logic_ will be familiar, between\nan inference drawn _according_ to a formula and one drawn\n_from_ a formula. We do in reality make our inference from\nthe data afforded by experience directly to the conclusion;\nit is a mere arrangement of convenience to do so by passing\nthrough the generalization. But it is one of such extreme\nconvenience, and one so necessarily forced upon us when we\nare appealing to our own past experience or to that of others\nfor the grounds of our conclusion, that practically we find it\nthe best plan to divide the process of inference into two\nparts. The first part is concerned with establishing the\ngeneralization; the second (which contains the rules of ordinary\nlogic) determines what conclusions can be drawn from\nthis generalization.\n\n6. We may now see our way to ascertaining the province\nof Probability and its relation to kindred sciences.\nInductive Logic gives rules for discovering such generalizations\nas those spoken of above, and for testing their correctness.\nIf they are expressed in universal propositions it is\nthe part of ordinary logic to determine what inferences can\nbe made from and by them; if, on the other hand, they are\nexpressed in proportional propositions, that is, propositions\nof the kind described in our first chapter, they are handed\nover to Probability. We find, for example, that three infants\nout of ten die in their first four years. It belongs to Induction\nto say whether we are justified in generalizing our observation\ninto the assertion, All infants die in that proportion.\nWhen such a proposition is obtained, whatever may be the\nvalue to be assigned to it, we recognize in it a series of a\nfamiliar kind, and it is at once claimed by Probability.\n\nIn this latter case the division into two parts, the inductive\nand the ratiocinative, seems decidedly more than one of\nconvenience; it is indeed imperatively necessary for clearness\nof thought and cogency of treatment. It is true that in\nalmost every example that can be selected we shall find\nboth of the above elements existing together and combining\nto determine the degree of our conviction, but when we come\nto examine them closely it appears to me that the grounds\nof their cogency, the kind of conviction they produce, and\nconsequently the rules which they give rise to, are so entirely\ndistinct that they cannot possibly be harmonized into\na single consistent system.\n\nThe opinion therefore according to which certain Inductive\nformul\u00e6 are regarded as composing a portion of\nProbability, and which finds utterance in the Rule of Succession\ncriticised in our last chapter, cannot, I think, be\nmaintained. It would be more correct to say, as stated\nabove, that Induction is quite distinct from Probability, yet\nco-operates in almost all its inferences. By Induction we\ndetermine, for example, whether, and how far, we can safely\ngeneralize the proposition that four men in ten live to be\nfifty-six; supposing such a proposition to be safely generalized,\nwe hand it over to Probability to say what sort of inferences\ncan be deduced from it.\n\n7. So much then for the opinion which tends to regard\npure Induction as a subdivision of Probability. By the\nmajority of philosophical and logical writers a widely different\nview has of course been entertained. They are mostly disposed\nto distinguish these sciences very sharply from, not to\nsay to contrast them with, one another; the one being\naccepted as philosophical or logical, and the other rejected\nas mathematical. This may without offence be termed the\npopular prejudice against Probability.\n\nA somewhat different view, however, must be noticed\nhere, which, by a sort of reaction against the latter, seems\neven to go beyond the former; and which occasionally finds\nexpression in the statement that all inductive reasoning of\nevery kind is merely a matter of Probability. Two examples\nof this may be given.\n\nBeginning with the older authority, there is an often\nquoted saying by Butler at the commencement of his _Analogy_,\nthat 'probability is the very guide of life'; a saying\nwhich seems frequently to be understood to signify that the\nrules or principles of Probability are thus all-prevalent when\nwe are drawing conclusions in practical life. Judging by\nthe drift of the context, indeed, this seems a fair interpretation\nof his meaning, in so far of course as there could\nbe said to be any such thing as a science of Probability in\nthose days. Prof. Jevons, in his _Principles of Science_\n(p. 197), has expressed a somewhat similar view, of course\nin a way more consistent with the principles of modern\nscience, physical and mathematical. He says, \"I am convinced\nthat it is impossible to expound the methods of induction\nin a sound manner, without resting them on the\ntheory of Probability. Perfect knowledge alone can give\ncertainty, and in nature perfect knowledge would be infinite\nknowledge, which is clearly beyond our capacities. We have,\ntherefore, to content ourselves with partial knowledge,--knowledge\nmingled with ignorance, producing doubt.\"[2]\n\n8. There are two senses in which this disposition to\nmerge the two sciences into one may be understood. Using\nthe word Probability in its vague popular signification,\nnothing more may be intended than to call attention to the\nfact, that in every case alike our conclusions are nothing\nmore than 'probable,' that is, that they are not, and cannot\nbe, absolutely certain. This must be fully admitted, for of\ncourse no one acquainted with the complexity of physical\nand other evidence would seriously maintain that absolute\nideal certainty can be attained in any branch of applied\nlogic. Hypothetical certainty, in abstract science, may be\npossible, but not absolute certainty in the domain of the\nconcrete. This has been already noticed in a former chapter,\nwhere, however, it was pointed out that whatever justification\nmay exist, on the subjective view of logic, for regarding\nthis common prevalence of absence of certainty as warranting\nus in fusing the sciences into one, no such justification is\nadmitted when we take the objective view.\n\n9. What may be meant, however, is that the _grounds_\nof this absence of certainty are always of the same general\ncharacter. This argument, if admitted, would have real\nforce, and must therefore be briefly noticed. We have seen\nabundantly that when we say of a conclusion within the\nstrict province of Probability, that it is not certain, all that\nwe mean is that in some proportion of cases only will such\nconclusion be right, in the other cases it will be wrong.\nNow when we say, in reference to any inductive conclusion,\nthat we feel uncertain about its absolute cogency, are we\nconscious of the same interpretation? It seems to me that\nwe are not. It is indeed quite possible that on ultimate\nanalysis it might be proved that experience of failure in\nthe past employment of our methods of investigation was\nthe main cause of our present want of perfect confidence in\nthem. But this, as we have repeatedly insisted, does not\nbelong to the province of logical, but to that of Psychological\nenquiry. It is surely not the case that we are, as a rule,\nconsciously guided by such occasional or repeated instances\nof past failure. In so far as they are at all influential, they\nseem to do their work by infusing a vague want of confidence\nwhich cannot be referred to any statistical grounds for\nits justification, at least not in a quantitative way. Part of\nour want of confidence is derived sympathetically from those\nwho have investigated the matter more nearly at first hand.\nHere again, analysis might detect that a given proportion of\npast failures lay at the root of the distrust, but it does not\nshow at the surface. Moreover, one reason why we cannot\nfeel perfectly certain about our inductions is, that the\n_memory_ has to be appealed to for some of our data; and will\nany one assert that the only reason why we do not place\nabsolute reliance on our memory of events long past is that\nwe have been deceived in that way before?\n\nIn any other sense, therefore, than as a needful protest\nagainst attaching too great demonstrative force to the conclusions\nof Inductive Logic, it seems decidedly misleading to\nspeak of its reasonings as resting upon Probability.\n\n10. We may now see clearly the reasons for the\nlimits within which causation[3] is necessarily required, but\nbeyond which it is not needed. To be able to generalize\na formula so as to extend it from the observed to the unobserved,\nit is clearly essential that there should be a certain\npermanence in the order of nature; this permanence is one\nform of what is implied in the term causation. If the\ncircumstances under which men live and die remaining the\nsame, we did not feel warranted in inferring that four men\nout of ten would continue to live to fifty, because in the case\nof those whom we had observed this proportion had hitherto\ndone so, it is clear that we should be admitting that the\nsame antecedents need not be followed by the same consequents.\nThis uniformity being what the Law of Causation\nasserts, the truth of the law is clearly necessary to enable us\nto obtain our generalizations: in other words, it is necessary\nfor the Inductive part of the process. But it seems to be\nequally clear that causation is not necessary for that part of\nthe process which belongs to Probability. Provided only\nthat the truth of our generalizations is secured to us, in the\nway just mentioned, what does it matter to us whether or\nnot the individual members are subject to causation? For\nit is not in reality about these individuals that we make\ninferences. As this last point has been already fully treated\nin Chapter VI., any further allusion to it need not be made here.\n\n11. The above description, or rather indication, of the\nprocess of obtaining these generalizations must suffice for the\npresent. Let us now turn and consider the means by which\nwe are practically to make use of them when they are obtained.\nThe point which we had reached in the course of the\ninvestigations entered into in the sixth and seventh chapters\nwas this:--Given a series of a certain kind, we could draw\ninferences about the members which composed it; inferences,\nthat is, of a peculiar kind, the value and meaning of which\nwere fully discussed in their proper place.\n\nWe must now shift our point of view a little; instead of\nstarting, as in the former chapters, with a determinate series\nsupposed to be given to us, let us assume that the individual\nonly is given, and that the work is imposed upon us of finding\nout the appropriate series. How are we to set about the\ntask? In the former case our data were of this kind:--Eight\nout of ten men, aged fifty, will live eleven years more,\nand we ascertained in what sense, and with what certainty,\nwe could infer that, say, John Smith, aged fifty, would live\nto sixty-one.\n\n12. Let us then suppose, instead, that John Smith\npresents himself, how should we in this case set about obtaining\na series for him? In other words, how should we\ncollect the appropriate statistics? It should be borne in\nmind that when we are attempting to make real inferences\nabout things as yet unknown, it is in this form that the\nproblem will practically present itself.\n\nAt first sight the answer to this question may seem to be\nobtained by a very simple process, viz. by counting how\nmany men of the age of John Smith, respectively do and do\nnot live for eleven years. In reality however the process is\nfar from being so simple as it appears. For it must be remembered\nthat each individual thing has not one distinct\nand appropriate class or group, to which, and to which alone,\nit properly belongs. We may indeed be practically in the\nhabit of considering it under such a single aspect, and it may\ntherefore seem to us more familiar when it occupies a place\nin one series rather than in another; but such a practice is\nmerely customary on our part, not obligatory. It is obvious\nthat every individual thing or event has an indefinite\nnumber of properties or attributes observable in it, and\nmight therefore be considered as belonging to an indefinite\nnumber of different classes of things. By belonging to any\none class it of course becomes at the same time a member of\nall the higher classes, the genera, of which that class was a\nspecies. But, moreover, by virtue of each accidental attribute\nwhich it possesses, it becomes a member of a class\nintersecting, so to say, some of the other classes. John Smith\nis a consumptive man say, and a native of a northern climate.\nBeing a man he is of course included in the class of vertebrates,\nalso in that of animals, as well as in any higher\nsuch classes that there may be. The property of being consumptive\nrefers him to another class, narrower than any of\nthe above; whilst that of being born in a northern climate\nrefers him to a new and distinct class, not conterminous with\nany of the rest, for there are things born in the north which\nare not men.\n\n13. When therefore John Smith presents himself to\nour notice without, so to say, any particular label attached to\nhim informing us under which of his various aspects he is to\nbe viewed, the process of thus referring him to a class becomes\nto a great extent arbitrary. If he had been indicated\nto us by a general name, that, of course, would have been\nsome clue; for the name having a determinate connotation\nwould specify at any rate a fixed group of attributes within\nwhich our selection was to be confined. But names and\nattributes being connected together, we are here supposed\nto be just as much in ignorance what name he is to be\ncalled by, as what group out of all his innumerable attributes\nis to be taken account of; for to tell us one of these things\nwould be precisely the same in effect as to tell us the other.\nIn saying that it is thus arbitrary under which class he is\nplaced, we mean, of course, that there are no logical grounds\nof decision; the selection must be determined by some extraneous\nconsiderations. Mere inspection of the individual\nwould simply show us that he could equally be referred\nto an indefinite number of classes, but would in itself give\nno inducement to prefer, for our special purpose, one of these\nclasses to another.\n\nThis variety of classes to which the individual may be\nreferred owing to his possession of a multiplicity of attributes,\nhas an important bearing on the process of inference\nwhich was indicated in the earlier sections of this chapter,\nand which we must now examine in more special reference\nto our particular subject.\n\n14. It will serve to bring out more clearly the nature\nof some of those peculiarities of the step which we are now\nabout to take in the case of Probability, if we first examine\nthe form which the corresponding step assumes in the case\nof ordinary Logic. Suppose then that we wished to ascertain\nwhether a certain John Smith, a man of thirty, who is\namongst other things a resident in India, and distinctly\naffected with cancer, will continue to survive there for\ntwenty years longer. The terms in which the man is thus\nintroduced to us refer him to different classes in the way\nalready indicated. Corresponding to these classes there will\nbe a number of propositions which have been obtained by\nprevious observations and inductions, and which we may\ntherefore assume to be available and ready at hand when\nwe want to make use of them. Let us conceive them to\nbe such as these following:--Some men live to fifty; some\nIndian residents live to fifty; no man suffering thus from\ncancer lives for five years. From the first and second of these\npremises nothing whatever can be inferred, for they are both[4]\nparticular propositions, and therefore lead to no conclusion\nin this case. The third answers our enquiry decisively.\n\nTo the logical reader it will hardly be necessary to point\nout that the process here under consideration is that of\nfinding middle terms which shall serve to connect the\nsubject and predicate of our conclusion. This subject and\npredicate in the case in question, are the individual before\nus and his death within the stated period. Regarded by\nthemselves there is nothing in common between them, and\ntherefore no link by which they may be connected or disconnected\nwith each other. The various classes above\nreferred to are a set of such middle terms, and the propositions\nbelonging to them are a corresponding set of major\npremises. By the help of any one of them we are enabled,\nunder suitable circumstances, to connect together the subject\nand predicate of the conclusion, that is, to infer whether the\nman will or will not live twenty years.\n\n15. Now in the performance of such a logical process\nthere are two considerations to which the reader's attention\nmust for a moment be directed. They are simple enough in\nthis case, but will need careful explanation in the corresponding\ncase in Probability. In the first place, it is clear that\nwhenever we can make any inference at all, we can do so\nwith absolute certainty. Logic, within its own domain,\nknows nothing of hesitation or doubt. If the middle term\nis appropriate it serves to connect the extremes in such a\nway as to preclude all uncertainty about the conclusion;\nif it is not, there is so far an end of the matter: no conclusion\ncan be drawn, and we are therefore left where we were.\nAssuming our premises to be correct, we either know our\nconclusion for certain, or we know nothing whatever about\nit. In the second place, it should be noticed that none of\nthe possible alternatives in the shape of such major premises\nas those given above can ever contradict any of the others,\nor be at all inconsistent with them. Regarded as isolated\npropositions, there is of course nothing to secure such harmony;\nthey have very different predicates, and may seem\nquite out of each other's reach for either support or opposition.\nBut by means of the other premise they are in each\ncase brought into relation with one another, and the general\ninterests of truth and consistency prevent them therefore\nfrom contradicting one another. As isolated propositions\nit might have been the case that all men live to fifty, and\nthat no Indian residents do so, but having recognised that\nsome men are residents in India, we see at once that these\npremises are inconsistent, and therefore that one or other\nof them must be rejected. In all applied logic this necessity\nof avoiding self-contradiction is so obvious and imperious\nthat no one would think it necessary to lay down the formal\npostulate that all such possible major premises are to be\nmutually consistent. To suppose that this postulate is not\ncomplied with, would be in effect to make two or more contradictory\nassumptions about matters of fact.\n\n16. But now observe the difference when we attempt\nto take the corresponding step in Probability. For ordinary\npropositions, universal or particular, substitute statistical\npropositions of what we have been in the habit of calling\nthe 'proportional' kind. In other words, instead of asking\nwhether the man will live for twenty years, let us ask whether\nhe will live for one year? We shall be unable to find any\nuniversal propositions which will cover the case, but we may\nwithout difficulty obtain an abundance of appropriate proportional\nones. They will be of the following description:--Of\nmen aged 30, 98 in 100 live another year; of residents in\nIndia a smaller proportion survive, let us for example say\n90 in 100; of men suffering from cancer a smaller proportion\nstill, let us say 20 in 100.\n\nNow in both of the respects to which attention has just\nbeen drawn, propositions of this kind offer a marked contrast\nwith those last considered. In the first place, they do\nnot, like ordinary propositions, either assert unequivocally\nyes or no, or else refuse to open their lips; but they give\ninstead a sort of qualified or hesitating answer concerning\nthe individuals included in them. This is of course nothing\nmore than the familiar characteristic of what may be called\n'probability propositions.' But it leads up to, and indeed\nrenders possible, the second and more important point;\nviz. that these various answers, though they cannot directly\nand formally contradict each other (this their nature as proportional\npropositions, will not as a rule permit), may yet, in\na way which will now have to be pointed out, be found to be\nmore or less in conflict with each other.\n\nHence it follows that in the attempt to draw a conclusion\nfrom premises of the kind in question, we may be placed\nin a position of some perplexity; but it is a perplexity\nwhich may present itself in two forms, a mild and an aggravated\nform. We will notice them in turn.\n\n17. The mild form occurs when the different classes\nto which the individual case may be appropriately referred\nare successively included one within another; for here our\nsets of statistics, though leading to different results, will\nnot often be found to be very seriously at variance with\none another. All that comes of it is that as we ascend in the\nscale by appealing to higher and higher genera, the statistics\ngrow continually less appropriate to the particular\ncase in point, and such information therefore as they afford\nbecomes gradually less explicit and accurate.\n\nThe question that we originally wanted to determine,\nbe it remembered, is whether John Smith will die within\none year. But all knowledge of this fact being unattainable,\nowing to the absence of suitable inductions, we felt\njustified (with the explanation, and under the restrictions\nmentioned in Chap VI.), in substituting, as the only available\nequivalent for such individual knowledge, the answer to the\nfollowing statistical enquiry, What proportion of men in his\ncircumstances die?\n\n18. But then at once there begins to arise some doubt\nand ambiguity as to what exactly is to be understood by his\ncircumstances. We may know very well what these circumstances\nare in themselves, and yet be in perplexity as to\nhow many of them we ought to take into account when\nendeavouring to estimate his fate. We might conceivably,\nfor a beginning, choose to confine our attention to those\nproperties only which he has in common with all animals.\nIf so, and statistics on the subject were attainable, they\nwould presumably be of some such character as this, Ninety-nine\nanimals out of a hundred die within a year. Unusual as\nsuch a reference would be, we should, logically speaking, be\ndoing nothing more than taking a wider class than the one\nwe were accustomed to. Similarly we might, if we pleased,\ntake our stand at the class of vertebrates, or at that of\nmammalia, if zoologists were able to give us the requisite\ninformation. Of course we reject these wide classes and\nprefer a narrower one. If asked why we reject them, the\nnatural answer is that they are so general, and resemble the\nparticular case before us in so few points, that we should be\nexceedingly likely to go astray in trusting to them. Though\naccuracy cannot be insured, we may at least avoid any needless\nexaggeration of the relative number and magnitude of\nour errors.\n\n19. The above answer is quite valid; but whilst cautioning\nus against appealing to too wide a class, it seems to\nsuggest that we cannot go wrong in the opposite direction,\nthat is in taking too narrow a class. And yet we do avoid\nany such extremes. John Smith is not only an Englishman;\nhe may also be a native of such a part of England, be living\nin such a Presidency, and so on. An indefinite number of\nsuch additional characteristics might be brought out into\nnotice, many of which at any rate have some bearing upon\nthe question of vitality. Why do we reject any consideration\nof these narrower classes? We do reject them, but it is for\nwhat may be termed a practical rather than a theoretical\nreason. As was explained in the first chapters, it is essential\nthat our series should contain a considerable number of terms\nif they are to be of any service to us. Now many of the\nattributes of any individual are so rare that to take them\ninto account would be at variance with the fundamental\nassumption of our science, viz. that we are properly concerned\nonly with the averages of large numbers. The more special\nand minute our statistics the better, provided only that we\ncan get enough of them, and so make up the requisite large\nnumber of instances. This is, however, impossible in many\ncases. We are therefore obliged to neglect one attribute\nafter another, and so to enlarge the contents of our class; at\nthe avowed risk of somewhat increased variety and unsuitability\nin the members of it, for at each step of this kind we\ndiverge more and more from the sort of instances that we\nreally want. We continue to do so, until we no longer gain\nmore in quantity than we lose in quality. We finally take\nour stand at the point where we first obtain statistics drawn\nfrom a sufficiently large range of observation to secure the\nrequisite degree of stability and uniformity.\n\n20. In such an example as the one just mentioned,\nwhere one of the successive classes--man--is a well-defined\nnatural kind or species, there is such a complete break in\neach direction at this point, that every one is prompted to\ntake his stand here. On the one hand, no enquirer would\never think of introducing any reference to the higher classes\nwith fewer attributes, such as animal or organized being:\nand on the other hand, the inferior classes, created by our\ntaking notice of his employment or place of residence, &c.,\ndo not as a rule differ sufficiently in their characteristics\nfrom the class _man_ to make it worth our while to attend\nto them.\n\nNow and then indeed these characteristics do rise into\nimportance, and whenever this is the case we concentrate\nour attention upon the class to which they correspond, that\nis, the class which is marked off by their presence. Thus,\nfor instance, the quality of consumptiveness separates any\none off so widely from the majority of his fellow-men in all\nquestions pertaining to mortality, that statistics about the\nlives of consumptive men differ materially from those which\nrefer to men in general. And we see the result; if a consumptive\nman can effect an insurance at all, he must do it\nfor a much higher premium, calculated upon his special\ncircumstances. In other words, the attribute is sufficiently\nimportant to mark off a fresh class or series. So with insurance\nagainst accident. It is not indeed attempted to\nmake a special rate of insurance for the members of each\nseparate trade, but the differences of risk to which they are\nliable oblige us to take such facts to some degree into\naccount. Hence, trades are roughly divided into two or\nthree classes, such as the ordinary, the hazardous, and the\nextra-hazardous, each having to pay its own rate of premium.\n\n21. Where one or other of the classes thus corresponds\nto natural kinds, or involves distinctions of co-ordinate importance\nwith those of natural kinds, the process is not\ndifficult; there is almost always some one of these classes\nwhich is so universally recognised to be the appropriate one,\nthat most persons are quite unaware of there being any\nnecessity for a process of selection. Except in the cases\nwhere a man has a sickly constitution, or follows a dangerous\nemployment, we seldom have occasion to collect statistics for\nhim from any class but that of men in general of his age in\nthe country.\n\nWhen, however, these successive classes are not ready\nmarked out for us by nature, and thence arranged in easily\ndistinguishable groups, the process is more obviously arbitrary.\nSuppose we were considering the chance of a man's\nhouse being burnt down, with what collection of attributes\nshould we rest content in this instance? Should we include\nall kinds of buildings, or only dwelling-houses, or confine\nourselves to those where there is much wood, or those which\nhave stoves? All these attributes, and a multitude of others\nmay be present, and, if so, they are all circumstances which\nhelp to modify our judgment. We must be guided here by\nthe statistics which we happen to be able to obtain in\nsufficient numbers. Here again, rough distinctions of this\nkind are practically drawn in Insurance Offices, by dividing\nrisks into ordinary, hazardous, and extra-hazardous. We\nexamine our case, refer it to one or other of these classes,\nand then form our judgment upon its prospects by the statistics\nappropriate to its class.\n\n22. So much for what may be called the mild form in\nwhich the ambiguity occurs; but there is an aggravated form\nin which it may show itself, and which at first sight seems\nto place us in far greater perplexity.\n\nSuppose that the different classes mentioned above are\nnot included successively one within the other. We may\nthen be quite at a loss which of the statistical tables to\nemploy. Let us assume, for example, that nine out of ten\nEnglishmen are injured by residence in Madeira, but that\nnine out of ten consumptive persons are benefited by such a\nresidence. These statistics, though fanciful, are conceivable\nand perfectly compatible. John Smith is a consumptive\nEnglishman; are we to recommend a visit to Madeira in his\ncase or not? In other words, what inferences are we to\ndraw about the probability of his death? Both of the statistical\ntables apply to his case, but they would lead us to\ndirectly contradictory conclusions. This does not mean, of\ncourse, contradictory precisely in the logical sense of that\nword, for one of these propositions does not assert that an\nevent must happen and the other deny that it must; but\ncontradictory in the sense that one would cause us in some\nconsiderable degree to believe what the other would cause us\nin some considerable degree to disbelieve. This refers, of\ncourse, to the individual events; the statistics are by supposition\nin no degree contradictory. Without further data,\ntherefore, we can come to no decision.\n\n23. Practically, of course, if we were forced to a decision\nwith only these data before us, we should make our\nchoice by the consideration that the state of a man's lungs\nhas probably more to do with his health than the place of\nhis birth has; that is, we should conclude that the duration\nof life of consumptive Englishmen corresponds much more\nclosely with that of consumptive persons in general than\nwith that of their healthy countrymen. But this is, of\ncourse, to import empirical considerations into the question.\nThe data, as they are given to us, and if we confine ourselves\nto them, leave us in absolute uncertainty upon the\npoint. It may be that the consumptive Englishmen almost\nall die when transported into the other climate; it may be\nthat they almost all recover. If they die, this is in obvious\naccordance with the first set of statistics; it will be found in\naccordance with the second set through the fact of the\nforeign consumptives profiting by the change of climate in\nmore than what might be termed their due proportion.\nA similar explanation will apply to the other alternative,\nviz. to the supposition that the consumptive Englishmen\nmostly recover. The problem is, therefore, left absolutely\nindeterminate, for we cannot here appeal to any general rule\nso simple and so obviously applicable as that which, in a\nformer case, recommended us always to prefer the more\nspecial statistics, when sufficiently extensive, to those which\nare wider and more general. We have no means here of\nknowing whether one set is more special than the other.\n\nAnd in this no difficulty can be found, so long as we\nconfine ourselves to a just view of the subject. Let me\nagain recall to the reader's mind what our present position\nis; we have substituted for knowledge of the individual\n(finding that unattainable) a knowledge of what occurs in\nthe average of similar cases. This step had to be taken the\nmoment the problem was handed over to Probability. But\nthe conception of similarity in the cases introduces us to a\nperplexity; we manage indeed to evade it in many instances,\nbut here it is inevitably forced upon our notice.\nThere are here two aspects of this similarity, and they\nintroduce us to two distinct averages. Two assertions are\nmade as to what happens in the long run, and both of these\nassertions, by supposition, are verified. Of their truth there\nneed be no doubt, for both were supposed to be obtained\nfrom experience.\n\n24. It may perhaps be supposed that such an example\nas this is a _reductio ad absurdum_ of the principle upon which\nLife and other Insurances are founded. But a moment's\nconsideration will show that this is quite a mistake, and\nthat the principle of insurance is just as applicable to\nexamples of this kind as to any other. An office need find\nno difficulty in the case supposed. They _might_ (for a reason\nto be mentioned presently, they probably _would_ not) insure\nthe individual without inconsistency at a rate determined\nby either average. They might say to him, \"You are an\nEnglishman. Out of the multitude of English who come to\nus nine in ten die if they go to Madeira. We will insure\nyou at a rate assigned by these statistics, knowing that in\nthe long run all will come right so far as we are concerned.\nYou are also consumptive, it is true, and we do not know\nwhat proportion of the English are consumptive, nor what\nproportion of English consumptives die in Madeira. But\nthis does not really matter for our purpose. The formula,\nnine in ten die, is in reality calculated by taking into account\nthese unknown proportions; for, though we do not know\nthem in themselves, statistics tell us all that we care to\nknow about their results. In other words, whatever unknown\nelements may exist, must, in regard to all the effects\nwhich they can produce, have been already taken into\naccount, so that our ignorance about them cannot in the\nleast degree invalidate such conclusions as we are able to\ndraw. And this is sufficient for our purpose.\" But precisely\nthe same language might be held to him if he presented\nhimself as a consumptive man; that is to say, the office\ncould safely carry on its proceedings upon either alternative.\n\nThis would, of course, be a very imperfect state for the\nmatter to be left in. The only rational plan would be to\nisolate the case of consumptive Englishmen, so as to make\na separate calculation for their circumstances. This calculation\nwould then at once supersede all other tables so\nfar as they were concerned; for though, _in the end_, it could\nnot arrogate to itself any superiority over the others, it\nwould in the mean time be marked by fewer and slighter\naberrations from the truth.\n\n25. The real reason why the Insurance office could\nnot long work on the above terms is of a very different\nkind from that which some readers might contemplate, and\nbelongs to a class of considerations which have been much\nneglected in the attempts to construct sciences of the different\nbranches of human conduct. It is nothing else than\nthat annoying contingency to which prophets since the time\nof Jonah have been subject, of uttering _suicidal_ prophecies;\nof publishing conclusions which are perfectly certain when\nevery condition and cause but one have been taken into\naccount, that one being the effect of the prophecy itself\nupon those to whom it refers.\n\nIn our example above, the office (in so far as the particular\ncases in Madeira are concerned) would get on very well\nuntil the consumptive Englishmen in question found out\nwhat much better terms they could make by announcing\nthemselves as consumptives, and paying the premium appropriate\nto that class, instead of announcing themselves as\nEnglishmen. But if they did this they would of course be\ndisturbing the statistics. The tables were based upon the\nassumption that a certain fixed proportion (it does not\nmatter what proportion) of the English lives would continue\nto be consumptive lives, which, under the supposed circumstances,\nwould probably soon cease to be true. When it is\nsaid that nine Englishmen out of ten die in Madeira, it is\nmeant that of those who come to the office, as the phrase is,\nat random, or in their fair proportions, nine-tenths die. The\nconsumptives are supposed to go there just like red-haired\nmen, or poets, or any other special class. Or they might go\nin any proportions greater or less than those of other classes,\nso long as they adhered to the same proportion throughout.\nThe tables are then calculated on the continuance of this\nstate of things; the practical contradiction is in supposing\nsuch a state of things to continue after the people had once\nhad a look at the tables. If we merely make the assumption\nthat the publication of these tables made no such alteration\nin the conduct of those to whom it referred, no hitch of\nthis kind need occur.\n\n26. The assumptions here made, as has been said, are\nnot in any way contradictory, but they need some explanation.\nIt will readily be seen that, taken together, they are\ninconsistent with the supposition that each of these classes is\nhomogeneous, that is, that the statistical proportions which\nhold of the whole of either of them will also hold of any\nportion of them which we may take. There are certain\nindividuals (viz. the consumptive Englishmen) who belong\nto each class, and of course the two different sets of statistics\ncannot both be true of them taken by themselves. They\nmight coincide in their characteristics with either class, but\nnot with both; probably in most practical cases they will\ncoincide with neither, but be of a somewhat intermediate\ncharacter. Now when it is said of any such heterogeneous\nbody that, say, nine-tenths die, what is meant (or rather\nimplied) is that the class might be broken up into smaller\nsubdivisions of a more homogeneous character, in some of\nwhich, of course, more than nine-tenths die, whilst in others\nless, the differences depending upon their character, constitution,\nprofession, &c.; the number of such divisions and the\namount of their divergence from one another being perhaps\nvery considerable.\n\nNow when we speak of either class as a whole and say\nthat nine-tenths die, the most natural and soundest meaning\nis that that would be the proportion if all without\nexception went abroad, or (what comes to the same thing) if\neach of these various subdivisions was represented in fair\nproportion to its numbers. Or it might only be meant that\nthey go in some other proportion, depending upon their\ntastes, pursuits, and so on. But whatever meaning be adopted\none condition is necessary, viz. that the proportion of each\nclass that went at the time the statistics were drawn up\nmust be adhered to throughout. When the class is homogeneous\nthis is not needed, but when it is heterogeneous the\nstatistics would be interfered with unless this condition were\nsecured.\n\nWe are here supposed to have two sets of statistics, one\nfor the English and one for the consumptives, so that the\nconsumptive English are in a sense counted twice over. If\ntheir mortality is of an intermediate amount, therefore, they\nserve to keep down the mortality of one class and to keep\nup that of the other. If the statistics are supposed to be\nexhaustive, by referring to the whole of each class, it follows\nthat actually the same individuals must be counted each\ntime; but if representatives only of each class are taken, the\nsame individuals need not be inserted in each set of tables.\n\n27. When therefore they come to insure (our remarks\nare still confined to our supposed Madeira case), we have\nsome English consumptives counted as English, and paying\nthe high rate; and others counted as consumptives and paying\nthe low rate. Logically indeed we may suppose them all\nentered in each class, and paying therefore each rate. What\nwe have said above is that any individual may be conceived\nto present himself for either of these classes. Conceive that\nsome one else pays his premium for him, so that it is a\nmatter of indifference to him personally at which rate he\ninsures, and there is nothing to prevent some of the class (or\nfor that matter all) going to one class, and others (or all\nagain) going to the other class.\n\nSo long therefore as we make the logically possible\nthough practically absurd supposition that some men will\ncontinue to pay a higher rate than they need, there is nothing\nto prevent the English consumptives (some or all) from\ninsuring in each category and paying its appropriate premium.\nAs soon as they gave any thought to the matter, of\ncourse they would, in the case supposed, all prefer to insure\nas consumptives. But their doing this would disturb each set\nof statistics. The English mortality in Madeira would instantly\nbecome heavier, so far as the Insurance company was\nconcerned, by the loss of all their best lives; whilst the consumptive\nstatistics (unless _all_ the English consumptives had\nalready been taken for insurance) would be in the same way\ndeteriorated.[5] A slight readjustment therefore of each scale\nof insurance would then be needed; this is the disturbance\nmentioned just above. It must be clearly understood, however,\nthat it is not our original statistics which have proved\nto be inconsistent, but simply that there were practical\nobstacles to carrying out a system of insurance upon them.\n\n28. Examples subject to the difficulty now under\nconsideration will doubtless seem perplexing to the student\nunacquainted with the subject. They are difficult to reconcile\nwith any other view of the science than that insisted on\nthroughout this Essay, viz. that we are only concerned with\naverages. It will perhaps be urged that there are two\ndifferent values of the man's life in these cases, and that\nthey cannot both be true. Why not? The 'value' of his\nlife is simply the number of years to which men in his\ncircumstances do, on the average, attain; we have the man\nset before us under two different circumstances; what wonder,\ntherefore, that these should offer different averages? In such\nan objection it is forgotten that we have had to substitute\nfor the unattainable result about the individual, the really\nattainable result about a set of men as much like him as\npossible. The difficulty and apparent contradiction only\narise when people will try to find some justification for their\nbelief in the individual case. What can we possibly conclude,\nit may be asked, about this particular man John\nSmith's prospects when we are thus offered two different\nvalues for his life? Nothing whatever, it must be replied;\nnor could we in reality draw a conclusion, be it remembered,\nin the former case, when we were practically confined to one\nset of statistics. There also we had what we called the\n'value' of his life, and since we only knew of one such value,\nwe came to regard it as in some sense appropriate to him as\nan individual. Here, on the other hand, we have two values,\nbelonging to different series, and as these values are really\ndifferent it may be complained that they are discordant, but\nsuch a complaint can only be made when we do what we\nhave no right to do, viz. assign a value to the individual\nwhich shall admit of individual justification.\n\n29. Is it then perfectly arbitrary what series or class\nof instances we select by which to judge? By no means; it\nhas been stated repeatedly that in choosing a series, we must\nseek for one the members of which shall resemble our individual\nin as many of his attributes as possible, subject only\nto the restriction that it must be a sufficiently extensive\nseries. What is meant is, that in the above case, where we\nhave two series, we cannot fairly call them contradictory; the\nonly valid charge is one of incompleteness or insufficiency for\ntheir purpose, a charge which applies in exactly the same\nsense, be it remembered, to all statistics which comprise\ngenera unnecessarily wider than the species with which we\nare concerned. The only difference between the two different\nclasses of cases is, that in the one instance we are on a\npath which we know will lead at the last, through many\nerrors, towards the truth (in the sense in which truth can be\nattained here), and we took it for want of a better. In the\nother instance we have two such paths, perfectly different\npaths, either of which however will lead us towards the truth\nas before. Contradiction can only seem to arise when it is\nattempted to justify each separate step on our paths, as well\nas their ultimate tendency.\n\nStill it cannot be denied that these objections are a\nserious drawback to the completeness and validity of any\nanticipations which are merely founded upon statistical frequency,\nat any rate in an early stage of experience, when\nbut few statistics have been collected. Such knowledge as\nProbability can give is not in any individual case of a high\norder, being subject to the characteristic infirmity of repeated\nerror; but even when measured by its own standard\nit commences at a very low stage of proficiency. The\nerrors are then relatively very numerous and large compared\nwith what they may ultimately be reduced to.\n\n30. Here as elsewhere there is a continuous process\nof specialization going on. The needs of a gradually widening\nexperience are perpetually calling upon us to subdivide\nclasses which are found to be too heterogeneous. Sometimes\nthe only complaint that has to be made is that the class to\nwhich we are obliged to refer is found to be somewhat too\nbroad to suit our purpose, and that it might be subdivided\nwith convenience. This is the case, as has been shown above,\nwhen an Insurance office finds that its increasing business\nmakes it possible and desirable to separate off the men who\nfollow some particular trades from the rest of their fellow-countrymen.\nSimilarly in every other department in which\nstatistics are made use of. This increased demand for specificness\nleads, in fact, as naturally in this direction, as does\nthe progress of civilization to the subdivision of trades in\nany town or country. So in reference to the other kind of\nperplexity mentioned above. Nothing is more common in\nthose sciences or practical arts, in which deduction is but\nlittle available, and where in consequence our knowledge is\nfor the most part of the empirical kind, than to meet with\nsuggestions which point more or less directly in contrary\ndirections. Whenever some new substance is discovered or\nbrought into more general use, those who have to deal with\nit must be familiar with such a state of things. The medical\nman who has to employ a new drug may often find himself\nconfronted by the two distinct recommendations, that on\nthe one hand it should be employed for certain diseases, and\nthat on the other hand it should not be tried on certain constitutions.\nA man with such a constitution, but suffering\nfrom such a disease, presents himself; which recommendation\nis the doctor to follow? He feels at once obliged to\nset to work to collect narrower and more special statistics,\nin order to escape from such an ambiguity.\n\n31. In this and a multitude of analogous cases\nafforded by the more practical arts it is not of course necessary\nthat numerical data should be quoted and appealed\nto; it is sufficient that the judgment is more or less consciously\ndetermined by them. All that is necessary to make\nthe examples appropriate is that we should admit that in\ntheir case statistical data are our ultimate appeal in the\npresent state of knowledge. Of course if the empirical\nlaws can be resolved into their component causes we may\nappeal to direct deduction, and in this case the employment\nof statistics, and consequently the use of the theory of\nProbability, may be superseded.\n\nIn this direction therefore, as time proceeds, the advance\nof statistical refinement by the incessant subdivision of classes\nto meet the developing wants of man is plain enough. But\nif we glance backwards to a more primitive stage, we shall\nsoon see in what a very imperfect state the operation commences.\nAt this early stage, however, Probability and Induction\nare so closely connected together as to be very apt to\nbe merged into one, or at any rate to have their functions\nconfounded.\n\n32. Since the generalization of our statistics is found to\nbelong to Induction, this process of generalization may be\nregarded as prior to, or at least independent of, Probability.\nWe have, moreover, already discussed (in Chapter VI.) the\nstep corresponding to what are termed immediate inferences,\nand (in Chapter VII.) that corresponding to syllogistic inferences.\nOur present position therefore is that in which we\nmay consider ourselves in possession of any number of generalizations,\nbut wish to employ them so as to make inferences\nabout a given individual; just as in one department of\ncommon logic we are engaged in finding middle terms to\nestablish the desired conclusion. In this latter case the\nprocess is found to be extremely simple, no accumulation of\ndifferent middle terms being able to lead to any real ambiguity\nor contradiction. In Probability, however, the case is\ndifferent. Here, if we attempt to draw inferences about the\nindividual case before us, as often is attempted--in the Rule\nof Succession for example--we shall encounter the full force\nof this ambiguity and contradiction. Treat the question,\nhowever, fairly, and all difficulty disappears. Our inference\nreally is not about the individuals as individuals, but about\nseries or successions of them. We wished to know whether\nJohn Smith will die within the year; this, however, cannot\nbe known. But John Smith, by the possession of many\nattributes, belongs to many different series. The multiplicity\nof middle terms, therefore, is what ought to be\nexpected. We _can_ know whether a succession of men, residents\nin India, consumptives, &c. die within a year. We\nmay make our selection, therefore, amongst these, and in the\nlong run the belief and consequent conduct of ourselves and\nother persons (as described in Chapter VI.) will become\ncapable of justification. With regard to choosing one of\nthese series rather than another, we have two opposing\nprinciples of guidance. On the one hand, the more special\nthe series the better; for, though not more right in the end,\nwe shall thus be more nearly right all along. But, on the\nother hand, if we try to make the series too special, we shall\ngenerally meet the practical objection arising from insufficient\nstatistics.\n\n\n1. Some of my readers may be familiar with a very striking digression\n  in Buffon's Natural History (_Natural Hist. of Man_, \u00a7VIII.), in\n  which he supposes the first man in full possession of his faculties,\n  but with all his experience to gain, and speculates on the gradual\n  acquisition of his knowledge. Whatever may be thought of his\n  particular conclusions the passage is very interesting and\n  suggestive to any student of Psychology.\n\n2. See also Dugald Stewart (Ed. by Hamilton; VII. pp. 115-119).\n\n3. Required that is for purposes of logical inference within the\n  limits of Probability; it is not intended to imply any doubts as to\n  its actual universal prevalence, or its all-importance for\n  scientific purposes. The subject is more fully discussed in a future\n  chapter.\n\n4. As particular propositions they are both of course identical in\n  form. The fact that the 'some' in the former corresponds to a\n  larger proportion than in the latter, is a distinction alien to pure\n  Logic.\n\n5. The reason is obvious. The healthiest English lives in Madeira\n  (viz. the consumptive ones) have now ceased to be reckoned as\n  English; whereas the worst consumptive lives there (viz. the\n  English) are now increased in relative numbers.\n\n\n\n\nCHAPTER X.\n\n\n_CHANCE AS OPPOSED TO CAUSATION AND DESIGN._\n\n1. The remarks in the previous chapter will have served\nto clear the way for an enquiry which probably excites more\npopular interest than any other within the range of our subject,\nviz. the determination whether such and such events are to\nbe attributed to Chance on the one hand, or to Causation or\nDesign on the other. As the principal difficulty seems to\narise from the ambiguity with which the problem is generally\nconceived and stated, owing to the extreme generality of the\nconceptions involved, it becomes necessary to distinguish\nclearly between the several distinct issues which are apt to\nbe involved.\n\nI. There is, to begin with, a very old objection, founded\non the assumption which our science is supposed to make of\nthe existence of _Chance_. The objection against chance is\nof course many centuries older than the Theory of Probability;\nand as it seems a nearly obsolete objection at the\npresent day we need not pause long for its consideration.\nIf we spelt the word with a capital C, and maintained that\nit was representative of some distinct creative or administrative\nagency, we should presumably be guilty of some form\nof Manicheism. But the only rational meaning of the objection\nwould appear to be that the principles of the science\ncompel us to assume that events (some events, only, that is)\nhappen without causes, and are thereby removed from the\ncustomary control of the Deity. As repeatedly pointed out\nalready this is altogether a mistake. The science of Probability\nmakes no assumption whatever about the way in\nwhich events are brought about, whether by causation or\nwithout it. All that we undertake to do is to establish and\nexplain a body of rules which are applicable to classes of\ncases in which we do not or cannot make inferences about\nthe individuals. The objection therefore must be somewhat\ndifferently stated, and appears finally to reduce itself\nto this:--that the assumptions upon which the science of\nProbability rests, are not inconsistent with a disbelief in\ncausation within certain limits; causation being of course\nunderstood simply in the sense of regular sequence. So\nstated the objection seems perfectly valid, or rather the facts\non which it is based must be admitted; though what connection\nthere would be between such lack of causation and\nabsence of Divine superintendence I quite fail to see.\n\nAs this Theological objection died away the men of\nphysical science, and those who sympathized with them,\nbegan to enforce the same protest; and similar cautions are\nstill to be found from time to time in modern treatises.\nHume, for instance, in his short essay on _Probability_, commences\nwith the remark, \"though there be no such thing as\nchance in the world, our ignorance of the real cause of any\nevent has the same influence on the understanding, &c.\"\nDe Morgan indeed goes so far as to declare that \"the\nfoundations of the theory of Probability have ceased to exist\nin the mind that has formed the conception,\" \"that anything\never did happen or will happen without some particular\nreason why it should have been precisely what it was and\nnot anything else.\"[1] Similar remarks might be quoted from\nLaplace and others.\n\n2. In the particular form of the controversy above\nreferred to, and which is mostly found in the region of the\nnatural and physical sciences, the contention that chance\nand causation are irreconcileable occupies rather a defensive\nposition; the main fact insisted on being that, whenever in\nthese subjects we may happen to be ignorant of the details\nwe have no warrant for assuming as a consequence that the\ndetails are uncaused. But this supposed irreconcileability\nis sometimes urged in a much more aggressive spirit in reference\nto social enquiries. Here the attempt is often made to\nprove causation in the details, from the known and admitted\nregularity in the averages. A considerable amount of controversy\nwas excited some years ago upon this topic, in great\npart originated by the vigorous and outspoken support of the\nnecessitarian side by Buckle in his _History of Civilization_.\n\nIt should be remarked that in these cases the attempt is\nsometimes made as it were to startle the reader into acquiescence\nby the singularity of the examples chosen. Instances\nare selected which, though they possess no greater logical\nvalue, are, if one may so express it, emotionally more effective.\nEvery reader of Buckle's History, for instance, will remember\nthe stress which he laid upon the observed fact, that the number\nof suicides in London remains about the same, year by year;\nand he may remember also the sort of panic with which the\npromulgation of this fact was accompanied in many quarters.\nSo too the way in which Laplace notices that the number of\nundirected letters annually sent to the Post Office remains\nabout the same, and the comments of Dugald Stewart upon\nthis particular uniformity, seem to imply that they regarded\nthis instance as more remarkable than many analogous ones\ntaken from other quarters.\n\nThat there is a certain foundation of truth in the reasonings\nin support of which the above examples are advanced,\ncannot be denied, but their authors appear to me very much\nto overrate the sort of opposition that exists between the\ntheory of Chances and the doctrine of Causation. As regards\nfirst that wider conception of order or regularity which we\nhave termed uniformity, anything which might be called\nobjective chance would certainly be at variance with this in\none respect. In Probability ultimate regularity is always\npostulated; in tossing a die, if not merely the individual\nthrows were uncertain in their results, but even the average\nalso, owing to the nature of the die, or the number of the\nmarks upon it, being arbitrarily interfered with, of course no\nkind of science would attempt to take any account of it.\n\n3. So much must undoubtedly be granted; but must\nthe same admission be made as regards the succession of the\nindividual events? Can causation, in the sense of invariable\nsuccession (for we are here shifting on to this narrower\nground), be denied, not indeed without suspicion of scientific\nheterodoxy, but at any rate without throwing uncertainty\nupon the foundations of Probability? De Morgan, as we\nhave seen, strongly maintains that this cannot be so. I find\nmyself unable to agree with him here, but this disagreement\nsprings not so much from differences of detail, as from those\nof the point of view in which we regard the science. He\nalways appears to incline to the opinion that the individual\njudgment in probability is to admit of justification;\nthat when we say, for instance, that the odds in favour of\nsome event are three to two, that we can explain and justify\nour statement without any necessary reference to a series or\nclass of such events. It is not easy to see how this can be\ndone in any case, but the obstacles would doubtless be\ngreater even than they are, if knowledge of the individual\nevent were not merely unattained, but, owing to the absence\nof any causal connection, essentially unattainable. On the\ntheory adopted in this work we simply postulate ignorance\nof the details, but it is not regarded as of any importance\non what sort of grounds this ignorance is based. It may\nbe that knowledge is out of the question from the nature\nof the case, the causative link, so to say, being missing. It\nmay be that such links are known to exist, but that either\nwe cannot ascertain them, or should find it troublesome to\ndo so. It is the fact of this ignorance that makes us appeal\nto the theory of Probability, the grounds of it are of no\nimportance.\n\n4. On the view here adopted we are concerned only\nwith averages, or with the single event as deduced from an\naverage and conceived to form one of a series. We start\nwith the assumption, grounded on experience, that there is\nuniformity in this average, and, so long as this is secured to\nus, we can afford to be perfectly indifferent to the fate, as\nregards causation, of the individuals which compose the\naverage. The question then assumes the following form:--Is\nthis assumption, of average regularity in the aggregate,\ninconsistent with the admission of what may be termed\ncauseless irregularity in the details? It does not seem to me\nthat it would be at all easy to prove that this is so. As\na matter of fact the two beliefs have constantly co-existed in\nthe same minds. This may not count for much, but it suggests\nthat if there be a contradiction between them it is by\nno means palpable and obvious. Millions, for instance, have\nbelieved in the general uniformity of the seasons taken one\nwith another, who certainly did not believe in, and would\nvery likely have been ready distinctly to deny, the existence\nof necessary sequences in the various phenomena which compose\nwhat we call a season. So with cards and dice; almost\nevery gambler must have recognized that judgment and\nforesight are of use in the long run, but writers on chance\nseem to think that gamblers need a good deal of reasoning to\nconvince them that each separate throw is in its nature essentially\npredictable.\n\n5. In its application to moral and social subjects,\nwhat gives this controversy its main interest is its real or\nsupposed bearing upon the vexed question of the freedom\nof the will; for in this region Causation, and Fatalism or\nNecessitarianism, are regarded as one and the same thing.\n\nHere, as in the last case, that wide and somewhat vague\nkind of regularity that we have called Uniformity, must be\nadmitted as a notorious fact. Statistics have put it out of\nthe power of any reasonably informed person to feel any\nhesitation upon this point. Some idea has already been\ngained, in the earlier chapters, of the nature and amount\nof the evidence which might be furnished of this fact, and\nany quantity more might be supplied from the works of\nprofessed writers upon the subject. If, therefore, Free-will be\nso interpreted as to imply such essential irregularity as defies\nprediction both in the average, and also in the single case,\nthen the negation of free-will follows, not as a remote logical\nconsequence, but as an obvious inference from indisputable\nfacts of experience.\n\nFew persons, however, would go so far as to interpret it\nin this sense. All that troubles them is the fear that somehow\nthis general regularity may be found to carry with it\ncausation, certainly in the sense of regular invariable sequence,\nand probably also with the further association of\ncompulsion. Rejecting the latter association as utterly\nunphilosophical, I cannot even see that the former consequence\ncan be admitted as really proved, though it doubtless\ngains some confirmation from this source.\n\n6. The nature of the argument against free-will,\ndrawn from statistics, at least in the form in which it is very\ncommonly expressed, seems to me exceedingly defective.\nThe antecedents and consequents, in the case of our volitions,\nmust clearly be supposed to be very nearly _immediately_\nin succession, if anything approaching to causation is to be\nestablished: whereas in statistical enquiries the data are\noften widely separate, if indeed they do not apply merely\nto single groups of actions or results. For instance, in the\ncase of the misdirected letters, what it is attempted to prove\nis that each writer was so much the 'victim of circumstances'\n(to use a common but misleading expression) that he could\nnot have done otherwise than he did under his circumstances.\nBut really no accumulation of figures to prove that the\nnumber of such letters remains the same year by year, can\nhave much bearing upon this doctrine, even though they\nwere accompanied by corresponding figures which should\nconnect the forgetfulness thus indicated with some other\ncharacteristics in the writers. So with the number of\nsuicides. If 250 people do, or lately did, annually put an\nend to themselves in London, the fact, as it thus stands by\nitself, may be one of importance to the philanthropist and\nstatesman, but it needs bringing into much closer relation\nwith psychological elements if it is to convince us that the\nactions of men are always instances of inflexible order. In\nfact, instead of having secured our A and B here in closest\nintimacy of succession to one another,--to employ the symbolic\nnotation commonly used in works on Inductive Logic\nto illustrate the causal connection,--we find them separated\nby a considerable interval; often indeed we merely\nhave an A or a B by itself.\n\n7. Again, another deficiency in such reasoning seems\nto be the laying undue weight upon the mere regularity or\npersistency of the statistics. These may lead to very important\nresults, but they are not exactly what is wanted\nfor the purpose of proving anything against the freedom\nof the will; it is not indeed easy to see what connection\nthis has with such facts as that the annual number of thefts\nor of suicides remains at pretty nearly the same figure.\nStatistical uniformity seems to me to establish nothing else,\nat least directly, in the case of human actions, than it does\nin that of physical characteristics. Take but one instance,\nthat of the misdirected letters. We were already aware\nthat the height, weight, chest measurement, and so on, of\na large number of persons preserved a tolerably regular\naverage amidst innumerable deflections, and we were prepared\nby analogy to anticipate the same regularity in their\nmental characteristics. All that we gain, by counting the\nnumbers of letters which are posted without addresses, is\na certain amount of direct evidence that this is the case.\nJust as observations of the former kind had already shown\nthat statistics of the strength and stature of the human\nbody grouped themselves about a mean, so do those of the\nlatter that a similar state of things prevails in respect of the\nreadiness and general trustworthiness of the memory. The\nevidence is not so direct and conclusive in the latter case,\nfor the memory is not singled out and subjected to measurement\nby itself, but is taken in combination with innumerable\nother influencing circumstances. Still there can be little\ndoubt that the statistics tell on the whole in this direction,\nand that by duly varying and extending them they may\nobtain considerable probative force.\n\nThe fact is that Probability has nothing more to do with\nNatural Theology, either in its favour or against it, than the\ngeneral principles of Logic or Induction have. It is simply a\nbody of rules for drawing inferences about classes of events\nwhich are distinguished by a certain quality. The believer\nin a Deity will, by the study of nature, be led to form an\nopinion about His works, and so to a certain extent about\nHis attributes. But it is surely unreasonable to propose\nthat he should abandon his belief because the sequence of\nevents,--not, observe, their general tendency towards happiness\nor misery, good or evil,--is brought about in a way\ndifferent from what he had expected; whether it be by displaying\norder where he had expected irregularity, or by\ninvolving the machinery of secondary causes where he had\nexpected immediate agency.\n\n8. It is both amusing and instructive to consider\nwhat very different feelings might have been excited in our\nminds by this co-existence of, what may be called, ignorance\nof individuals and knowledge of aggregates, if they had presented\nthemselves to our observation in a reverse order.\nBeing utterly unable to make assured predictions about a\nsingle life, or the conduct of individuals, people are sometimes\nstartled, and occasionally even dismayed, at the unexpected\ndiscovery that such predictions can be confidently\nmade when we are speaking of large numbers. And so\nsome are prompted to exclaim, This is denying Providence!\nit is utter Fatalism! But let us assume, for a moment, that\nour familiarity with the subject had been experienced, in the\nfirst instance, in reference to the aggregates instead of the\nindividual lives. It is difficult, perhaps, to carry out such a\nsupposition completely; though we may readily conceive\nsomething approaching to it in the case of an ignorant clerk\nin a Life Assurance Office, who had never thought of life, except\nas having such a 'value' at such an age, and who had\nhardly estimated it except in the form of averages. Might\nwe not suppose him, in some moment of reflectiveness, being\nastonished and dismayed at the sudden realization of the\nutter uncertainty in which the single life is involved? And\nmight not his exclamation in turn be, Why this is denying\nProvidence! It is utter chaos and chance! A belief in a\nCreator and Administrator of the world is not confined to\nany particular assumption about the nature of the immediate\nsequence of events, but those who have been accustomed\nhitherto to regard the events under one of the aspects above\nreferred to, will often for a time feel at a loss how to connect\nthem with the other.\n\n9. So far we have been touching on a very general\nquestion; viz. the relation of the fundamental postulates of\nProbability to the conception of Order or Uniformity in the\nworld, physical or moral. The difficulties which thence arise\nare mainly theological, metaphysical or psychological. What\nwe must now consider are problems of a more detailed or\nlogical character. They are prominently these two; (1) the\ndistinction between chance arrangement and _causal_ arrangement\nin physical phenomena; and (2) the distinction between\nchance arrangement and _designed_ arrangement where\nwe are supposed to be contemplating rational agency as\nacting on one side at least.\n\nII. The first of these questions raises the antithesis\nbetween chance and causation, not as a general characteristic\npervading all phenomena, but in reference to some specified\noccurrence:--Is this a case of chance or not? The most\nstrenuous supporters of the universal prevalence of causation\nand order admit that the question is a relevant one, and\nthey must therefore be supposed to have some rule for\ntesting the answers to it.\n\nSuppose, for instance, a man is seized with a fit in a\nhouse where he has gone to dine, and dies there; and some\none remarks that that was the very house in which he was\nborn. We begin to wonder if this was an odd coincidence\nand nothing more. But if our informant goes on to tell us\nthat the house was an old family one, and was occupied by\nthe brother of the deceased, we should feel at once that\nthese facts put the matter in a rather different light. Or\nagain, as Cournot suggests, if we hear that two brothers\nhave been killed in battle on the same day, it makes a great\ndifference in our estimation of the case whether they were\nkilled fighting in the same engagement or whether one fell\nin the north of France and the other in the south. The\nlatter we should at once class with mere coincidences, whereas\nthe former might admit of explanation.\n\n10. The problem, as thus conceived, seems to be one\nrather of Inductive Logic than of Probability, because there\nis not the slightest attempt to calculate chances. But it\ndeserves some notice here. Of course no accurate thinker\nwho was under the sway of modern physical notions would\nfor a moment doubt that each of the two elements in question\nhad its own 'cause' behind it, from which (assuming perfect\nknowledge) it might have been confidently inferred. No\nmore would he doubt, I apprehend, that if we could take a\nsufficiently minute and comprehensive view, and penetrate\nsufficiently far back into the past, we should reach a stage at\nwhich (again assuming perfect knowledge) the co-existence of\nthe two events could equally have been foreseen. The\nemployment of the word _casual_ therefore does not imply any\nrejection of a cause; but it does nevertheless correspond to a\ndistinction of some practical importance. We call a coincidence\ncasual, I apprehend, when we mean to imply that no\nknowledge of one of the two elements, which we can suppose\nto be practically attainable, would enable us to expect the\nother. We know of no generalization which covers them\nboth, except of course such as are taken for granted to be\ninoperative. In such an application it seems that the word\n'casual' is not used in antithesis to 'causal' or to 'designed',\nbut rather to that broader conception of order or regularity\nto which I should apply the term Uniformity. The casual\ncoincidence is one which we cannot bring under any special\ngeneralization; certain, probable, or even plausible.\n\nA slightly different way of expressing this distinction is\nto regard these 'mere coincidences' as being simply cases in\npoint of _independent_ events, in the sense in which independence\nwas described in a former chapter. We saw\nthat any two events, A and B, were so described when each\nhappens with precisely the same relative statistical frequency\nwhether the other happens or not. This state of things\nseems to hold good of the successions of heads and tails in\ntossing coins, as in that of male and female births in a\ntown, or that of the digits in many mathematical tables.\nThus we suppose that when men are picked up in the street\nand taken into a house to die, there will not be in the long\nrun any preferential selection for or against the house in\nwhich they were born. And all that we necessarily mean to\nclaim when we deny of such an occurrence, in any particular\ncase, that it is a mere coincidence, is that that particular\ncase must be taken out of the common list and transferred\nto one in which there _is_ some such preferential selection.\n\n11. III. The next problem is a somewhat more intricate\none, and will therefore require rather careful subdivision.\nIt involves the antithesis between Chance and\nDesign. That is, we are not now (as in the preceding case)\nconsidering objects in their physical aspect alone, and taking\naccount only of the relative frequency of their co-existence or\nsequence; but we are considering the agency by which they\nare produced, and we are enquiring whether that agency\ntrusted to what we call chance, or whether it employed what\nwe call design.\n\nThe reader must clearly understand that we are not now\ndiscussing the mere question of fact whether a certain\nassigned arrangement _is_ what we call a chance one. This,\nas was fully pointed out in the fourth chapter, can be settled\nby mere inspection, provided the materials are extensive\nenough. What we are now proposing to do is to carry on\nthe enquiry from the point at which we then had to leave it\noff, by solving the question, Given a certain arrangement, is\nit more likely that this was _produced_ by design, or by some\nof the methods commonly called chance methods? The distinction\nwill be obvious if we revert to the succession of\nfigures which constitute the ratio \u03c0. As I have said, this\narrangement, regarded as a mere succession of digits, appears\nto fulfil perfectly the characteristics of a chance arrangement.\nIf we were to omit the first four or five digits,\nwhich are familiar to most of us, we might safely defy any\none to whom it was shown to say that it was not got at by\nsimply drawing figures from a bag. He might look at it for\nhis whole life without detecting that it was anything but the\nresult of such a chance selection. And rightly so, because\nregarded as a mere arrangement it _is_ a chance one: it fulfils\nall the requirements of such an arrangement.[2] The question\nwe are now proceeding to discuss is this: Given any such\narrangement how are we to determine the process by which\nit was arrived at?\n\nWe are supposed to have some event before us which\nmight have been produced in either of two alternative\nways, i.e. by chance or by some kind of deliberate design;\nand we are asked to determine the odds in favour of one\nor other of these alternatives. It is therefore a problem in\nInverse Probability and is liable to all the difficulties to\nwhich problems of this class are apt to be exposed.\n\n12. For the theoretic solution of such a question we\nrequire the two following data:--\n\n(1) The relative frequency of the two classes of agencies,\nviz. that which is to act in a chance way and that which\nis to act designedly.\n\n(2) The probability that each of these agencies, if it\nwere the really operative one, would produce the event in\nquestion.\n\nThe latter of these data can generally be secured without\nany difficulty. The determination of the various contingencies\non the chance hypothesis ought not, if the example\nwere a suitable one, to offer any other than arithmetical\ndifficulties. And as regards the design alternative, it is\ngenerally taken for granted that if this had been operative\nit would certainly have produced the result aimed at. For\ninstance, if ten pence are found on a table, all with head\nuppermost, and it be asked whether chance or design had\nbeen at work here; we feel no difficulty up to a certain\npoint. Had the pence been tossed we should have got ten\nheads only once in 1024 throws; but had they been placed\ndesignedly the result would have been achieved with certainty.\n\nBut the other postulate, viz. that of the relative prevalence\nof these two classes of agencies, opens up a far more\nserious class of difficulties. Cases can be found no doubt,\nthough they are not very frequent, in which this question\ncan be answered approximately, and then there is no further\ntrouble. For instance, if in a school class-list I were to see\nthe four names Brown, Jones, Robinson, Smith, standing\nin this order, it might occur to me to enquire whether this\narrangement were alphabetical or one of merit. In our\nenlarged sense of the terms this is equivalent to chance\nand design as the alternatives; for, since the initial letter of\na boy's name has no known connection with his attainments,\nthe successive arrangement of these letters on any other\nthan the alphabetical plan will display the random features,\njust as we found to be the case with the digits of an incommensurable\nmagnitude. The odds are 23 to 1 against 4 names\ncoming undesignedly in alphabetical order; they are\nequivalent to certainty in favour of their doing so if this\norder had been designed. As regards the relative frequency\nof the two kinds of orders in school examinations I do not\nknow that statistics are at hand, though they could easily\nbe procured if necessary, but it is pretty certain that the\nmajority adopt the order of merit. Put for hypothesis the\nproportion as high as 9 to 1, and it would still be found more\nlikely than not that in the case in question the order was\nreally an alphabetical one.\n\n13. But in the vast majority of cases we have no\nsuch statistics at hand, and then we find ourselves exposed\nto very serious ambiguities. These may be divided into\ntwo distinct classes, the nature of which will best be seen\nby the discussion of examples.\n\nIn the first place we are especially liable to the drawback\nalready described in a former chapter as rendering\nmere statistics so untrustworthy, which consists in the fact\nthat the proportions are so apt to be disturbed almost from\nmoment to moment by the possession of fresh hints or information.\nWe saw for instance why it was that statistics of\nmortality were so very unserviceable in the midst of a\ndisease or in the crisis of a battle. Suppose now that on\ncoming into a room I see on the table ten coins lying face\nuppermost, and am asked what was the likelihood that the\narrangement was brought about by design. Everything\nturns upon special knowledge of the circumstances of the\ncase. Who had been in the room? Were they children,\nor coin-collectors, or persons who might have been supposed\nto have indulged in tossing for sport or for gambling purposes?\nWere the coins new or old ones? a distinction of\nthis kind would be very pertinent when we were considering\nthe existence of any motive for arranging them the same\nway uppermost. And so on; we feel that our statistics are\nat the mercy of any momentary fragment of information.\n\n14. But there is another consideration besides this.\nNot only should we be thus influenced by what may be\ncalled external circumstances of a general kind, such as the\ncharacter and position of the agents, we should also be influenced\nby what we supposed to be the conventional[3] estimate\nwith which this or that particular chance arrangement was\nthen regarded. Thus from time to time as new games of\ncards become popular new combinations acquire significance;\nand therefore when the question of design takes the form of\npossible cheating a knowledge of the current estimate of\nsuch combinations becomes exceedingly important.\n\n15. The full significance of these difficulties will best\nbe apprehended by the discussion of a case which is not\nfictitious or invented for the purpose, but which has actually\ngiven rise to serious dispute. Some years ago Prof. Piazzi\nSmyth published a work[4] upon the great pyramid of Ghizeh,\nthe general object of which was to show that that building\ncontained, in its magnitude, proportions and contents, a\nnumber of almost imperishable natural standards of length,\nvolume, &c. Amongst other things it was determined that\nthe value of \u03c0 was accurately (the degree of accuracy is not,\nI think, assigned) indicated by the ratio of the sides to the\nheight. The contention was that this result could not be\naccidental but must have been designed.\n\nAs regards the estimation of the value of the chance\nhypothesis the calculation is not quite so clear as in the\ncase of dice or cards. We cannot indeed suppose that,\nfor a given length of base, _any_ height can be equally possible.\nWe must limit ourselves to a certain range here; for if too\nhigh the building would be insecure, and if too low it would\nbe ridiculous. Again, we must decide to how close an\napproximation the measurements are made. If they are\nguaranteed to the hundredth of an inch the coincidence\nwould be of a quite different order from one where the\nguarantee extended only to an inch. Suppose that this\nhas been decided, and that we have ascertained that out\nof 10,000 possible heights for a pyramid of given base just\nthat one has been selected which would most nearly yield\nthe ratio of the radius to the circumference of a circle.\n\nThe remaining consideration would be the relative frequency\nof the 'design' alternative,--what is called its _\u00e0 priori_\nprobability,--that is, the relative frequency with\nwhich such builders can be supposed to have aimed at that\nratio; with the obvious implied assumption that if they did\naim at it they would certainly secure it. Considering our\nextreme ignorance of the attainments of the builders it is\nobvious that no attempt at numerical appreciation is here\npossible. If indeed the 'design' was interpreted to mean\nconscious resolve to produce that ratio, instead of mere resolve\nto employ some method which happened to produce\nit, few persons would feel much hesitation. Not only do\nwe feel tolerably certain that the builders did not know the\nvalue of \u03c0, except in the rude way in which all artificers\nmust know it; but we can see no rational motive, if they\ndid know it, which should induce them to perpetuate it\nin their building. If, however, to adopt an ingenious suggestion,[5]\nwe suppose that the builder may have proceeded\nin the following fashion, the matter assumes a different\naspect. Suppose that having decided on the height of his\npyramid he drew a circle with that as radius: that, laying\ndown a cord along the line of this circle, he drew this cord\nout into a square, which square marked the base of the\nbuilding. Hardly any simpler means could be devised in\na comparatively rude age; and it is obvious that the circumference\nof the base, being equal to the length of the\ncord, would bear exactly the admitted ratio to the height.\nIn other words, the exact attainment of a geometric value\ndoes not imply a knowledge of that ratio, but merely of some\nmethod which involves and displays it. A teredo can bore,\nas well as any of us, a hole which displays the geometric properties\nof a circle, but we do not credit it with corresponding\nknowledge.\n\nAs before said, all numerical appreciation of the likelihood\nof the design alternative is out of the question. But,\n_if_ the precision is equal to what Mr Smyth claimed, I suppose\nthat most persons (with the above suggestion before\nthem) will think it somewhat more likely that the coincidence\nwas not a chance one.\n\n16. There still remains a serious, and highly interesting\nspeculative consideration. In the above argument we took\nit for granted, in calculating the chance alternative, that\nonly _one_ of the 10,000 possible values was favourable; that\nis, we took it for granted that the ratio \u03c0 was the only one\nwhose claims, so to say, were before the court. But it is\nclear that if we had obtained just double this ratio the result\nwould have been of similar significance, for it would have\nbeen simply the ratio of the circumference to the diameter.\nIn fact, Mr Smyth's selected ratio,--the height to twice the\nbreadth of the base as compared with the diameter to the\ncircumference,--is obviously only one of a plurality of ratios.\nAgain; if the measured results had shown that the ratio of\nthe height to one side of the base was 1 : sqrt{2} (i.e. that of a\nside to a diagonal of a square) or 1 : sqrt{3} (i.e. that of a side\nto a diagonal of a cube) would not such results equally show\nevidence of design? Proceeding in this way, we might\nsuggest one known mathematical ratio after another until\nmost of the 10,000 supposed possible values had been taken\ninto account. We might then argue thus: since almost\nevery possible height of the pyramid would correspond to\n_some_ mathematical ratio, a builder, ignorant of them all\nalike, would be not at all unlikely to stumble upon one or\nother of them: why then attribute design to him in one case\nrather than another?\n\n17. The answer to this objection has been already\nhinted at. Everything turns upon the _conventional_ estimate\nof one result as compared with another. Revert, for simplicity\nto the coins. Ten heads is just as likely as alternate\nheads and tails, or five heads followed by five tails; or, in\nfact, as any one of the remaining 1023 possible cases. But\nuniversal convention has picked out a run of ten as being\nremarkable. Here, of course, the convention seems a very\nnatural and indeed inevitable one, but in other cases it is\nwholly arbitrary. For instance, in cards, \"queen of spades\nand knave of diamonds\" is exactly as uncommon as any\nother such pair: moreover, till _bezique_ was introduced it\noffered presumably no superior interest over any other\nspecified pair. But during the time when that game was\nvery popular this combination was brought into the category\nof coincidences in which interest was felt; and, given dishonesty\namongst the players, its chance of being designed\nstood at once on a much better footing.[6]\n\nReturning then to the pyramid, we see that in balancing\nthe claims of chance and design we must, in fairness to the\nlatter, reckon to its account several other values as well as\nthat of \u03c0, e.g. sqrt{2} and sqrt{3}, and a few more such simple and\nfamiliar ratios, as well as some of their multiples. But\nthough the number of such values which _might_ be reckoned,\non the ground that they are actually known to us, is infinite,\nyet the number that _ought_ to be reckoned, on the ground\nthat they could have been familiar to the builders of a\npyramid, are very few. The order of probability for or against\nthe existence of design will not therefore be seriously altered\nhere by such considerations.[7]\n\n18. Up to this point it will be observed that what we\nhave been balancing against each other are two forms of\nagency,--of human agency, that is,--one acting through\nchance, and the other by direct design. In this case we\nknow where we are, for we can thoroughly understand agency\nof this kind. The problem is indeed but seldom numerically\nsoluble, and in most cases not soluble at all, but it is at any\nrate capable of being clearly stated. We know the kind of\nanswer to be expected and the reasons which would serve to\ndetermine it, if they were attainable.\n\nThe next stage in the enquiry would be that of balancing\nordinary human chance agency against,--I will not call it\ndirect spiritualist agency, for that would be narrowing the\nhypothesis unnecessarily,--but against all other possible\ncauses. Some of the investigations of the Society for\nPsychical Research will furnish an admirable illustration of\nwhat is intended by this statement. There is a full discussion\nof these applications in a recent essay by Mr F. Y.\nEdgeworth;[8] but as his account of the matter is connected\nwith other calculations and diagrams I can only quote it in\npart. But I am in substantial agreement with him.\n\n\"It is recorded that 1833 guesses were made by a 'percipient'\nas to the suit of cards which the 'agent' had fixed\nupon. The number of successful guesses was 510, considerably\nabove 458, the number which, as being the quarter of 1833,\nwould, on the supposition of pure chance, be more\nlikely than any other number. Now, by the Law of Error,\nwe are able approximately to determine the probability of\nsuch an excess occurring by chance. It is equal to the extremity\nof the tail of a probability-curve such as [those we\n  have already had occasion to examine].... The proportion\nof this extremity of the tail to the whole body is 0.003 to 1.\nThat fraction, then, is the probability of a chance shot\nstriking that extremity of the tail; the probability that, if\nthe guessing were governed by pure chance, a number of\nsuccessful guesses equal or greater than 510 would occur\":\nodds, that is, of about 332 to 1 against such occurrence.\n\n19. Mr Edgeworth holds, as strongly as I do, that for purposes\nof calculation, in any strict sense of the word, we ought\nto have some determination of the data on the non-chance side\nof the hypothesis. We ought to know its relative frequency\nof occurrence, and the relative frequency with which it\nattains its aims. I am also in agreement with him that\n\"what that other cause may be,--whether some trick, or\nunconscious illusion, or _thought-transference_ of the sort which\nis vindicated by the investigators--it is for common-sense\nand ordinary Logic to consider.\"\n\nI am in agreement therefore with those who think that\nthough we cannot form a quantitative opinion we can in\ncertain cases form a tolerably decisive one. Of course if we\nallow the last word to the supporters of the chance hypothesis\nwe can never reach proof, for it will always be open to\nthem to revise and re-fix the antecedent probability of the\ncounter hypothesis. What we may fairly require is that\nthose who deny the chance explanation should assign some\nsort of minimum value to the probability of occurrence on\nthe other supposition, and we can then try to surmount this\nby increasing the rarity of the actually produced phenomenon\non the chance hypothesis. If, for instance, they declare that\nin their estimation the odds against any other than the chance\nagency being at work are greater than 332 to 1, we must\ntry to secure a yet uncommoner occurrence than that in\nquestion. If the supporters of thought-transference have\nthe courage of their convictions,--as they most assuredly\nhave,--they would not shrink from accepting this test. I\nam inclined to think that even at present, on such evidence\nas that above, the probability that the results were got at by\nordinary guessing is very small.\n\n20. The problems discussed in the preceding sections\nare at least intelligible even if they are not always resolvable.\nBut before finishing this chapter we must take notice\nof some speculations upon this part of the subject which do not\nseem to keep quite within the limits of what is intelligible.\nTake for instance the question discussed by Arbuthnott (in\na paper in the _Phil. Transactions_, Vol. XXVII.) under the\ntitle \"An Argument for Divine Providence, taken from the\nconstant Regularity observed in the birth of both sexes.\" Had\nhis argument been of the ordinary teleological kind; that\nis, had he simply maintained that the existent ratio of approximate\nequality, with a six per cent. surplusage of males,\nwas a beneficent one, there would have been nothing here to\nobject against. But what he contemplated was just such a\nbalance of alternate hypotheses between chance and design\nas we are here considering. His conclusion in his own words\nis, \"it is art, not chance, that governs.\"\n\nIt is difficult to render such an argument precise without\nrendering it simply ridiculous. Strictly understood it can\nsurely bear only one of two interpretations. On the one\nhand we may be personifying Chance: regarding it as an\nagent which must be reckoned with as being quite capable\nof having produced man, or at any rate having arranged the\nproportion of the sexes. And then the decision must be\ndrawn, as between this agent and the Creator, which of the\ntwo produced the existent arrangement. If so, and Chance\nbe defined as any agent which produces a chance or random\narrangement, I am afraid there can be little doubt that it\nwas this agent that was at work in the case in question.\nThe arrangement of male and female births presents, so far\nas we can see, one of the most perfect examples of chance:\nthere is ultimate uniformity emerging out of individual\nirregularity: all the 'runs' or successions of each alternative\nare duly represented: the fact of, say, five sons having been\nalready born in a family does not seem to have any certain\neffect in diminishing the likelihood of the next being a son,\nand so on. Such a nearly perfect instance of 'independent\nevents' is comparatively very rare in physical phenomena.\nIt is all that we can claim from a chance arrangement.[9] The\nonly other interpretation I can see is to suggest that there\nwas but one agent who might, like any one of us, have either\ntossed up or designed, and we have to ascertain which course\nhe probably adopted in the case in question. Here too, if\nwe are to judge of his mode of action by the tests we should\napply to any work of our own, it would certainly look very\nmuch as if he had adopted some scheme of tossing.\n\n21. The simple fact is that any rational attempt to\ndecide between chance and design as agencies must be confined\nto the case of finite intelligences. One of the important\ndetermining elements here, as we have seen, is the\nstate of knowledge of the agent, and the conventional estimate\nentertained about this or that particular arrangement;\nand these can be appreciated only when we are dealing with\nbeings like ourselves.\n\nFor instance, to return to that much debated question\nabout the arrangement of the stars, there can hardly be any\ndoubt that what Mitchell,--who started the discussion,--had\nin view was the decision between Chance and Design. He\nsays (_Trans. Roy. Soc._ 1767) \"The argument I intend to\nmake use of... is of that kind which infers either design or\nsome general law from a general analogy and from the greatness\nof the odds against things having been in the present\nsituation if it was not owing to some such cause.\" And he\nconcludes that had the stars \"been scattered by mere chance\nas it might happen\" there would be \"odds of near 500,000\nto 1 that no six stars out of that number [1500], scattered at\nrandom in the whole heavens, would be within so small a\ndistance from each other as the Pleiades are.\" Under any\nsuch interpretation the controversy seems to me to be idle.\nI do not for a moment dispute that there is some force in\nthe ordinary teleological argument which seeks to trace signs\nof goodness and wisdom in the general tendency of things.\nBut what do we possibly understand about the nature of\ncreation, or the designs of the Creator, which should enable\nus to decide about the likelihood of his putting the stars in\none shape rather than in another, or which should allow any\nsignificance to \"mere chance\" as contrasted with his supposed\nall-pervading agency?\n\n22. Reduced to intelligible terms the two following\nquestions seem to me to emerge from the controversy:--\n\n(I.) The stars being distributed through space, some of\nthem would of course be nearly in a straight line behind\nothers when looked at from our planet. Supposing that\nthey were tolerably uniformly distributed, we could calculate\nabout how many of them would thus be seen in apparent\nclose proximity to one another. The question is then put,\nAre there more of them near to each other, two and two,\nthan such calculation would account for? The answer is that\nthere are many more. So far as I can see the only direct\ninference that can be drawn from this is that they are _not_\nuniformly distributed, but have a tendency to go in pairs.\nThis, however, is a perfectly sound and reasonable application\nof the theory. Any further conclusions, such as that\nthese pairs of stars will form systems, as it were, to themselves,\nrevolving about one another, and for all practical purposes\nunaffected by the rest of the sidereal system, are of\ncourse derived from astronomical considerations.[10] Probability\nconfines itself to the simple answer that the distribution is\nnot uniform; it cannot pretend to say whether, and by what\nphysical process, these binary systems of stars have been\n'caused'.[11]\n\n23. (II.) The second question is this, Does the distribution\nof the stars, after allowing for the case of the binary\nstars just mentioned, resemble that which would be produced\nby human agency sprinkling things 'at random'?\n(We are speaking, of course, of their distribution as it appears\nto us, on the visible heavens, for this is nearly all that\nwe can observe; but if they extend beyond the telescopic\nrange in every direction, this would lead to practically much\nthe same discussion as if we considered their actual arrangement\nin space.) We have fully discussed, in a former chapter,\nthe meaning of 'randomness.' Applying it to the case\nbefore us, the question becomes this, Is the distribution\ntolerably uniform on the whole, but with innumerable individual\ndeflections? That is, when we compare large areas,\nare the ratios of the number of stars in each equal area\napproximately equal, whilst, as we compare smaller and\nsmaller areas, do the relative numbers become more and\nmore irregular? With certain exceptions, such as that of\nthe Milky Way and other nebular clusters, this seems to be\npretty much the case, at any rate as regards the bulk of the\nstars.[12]\n\nAll further questions: the decision, for instance, for or\nagainst any form of the Nebular Hypothesis: or, admitting\nthis, the decision whether such and such parts of the visible\nheavens have sprung from the same nebula, must be left to\nAstronomy to adjudicate.\n\n\nNOTE ON THE PROPORTIONS OF THE SEXES.\n\nThe following remarks were rather too long for convenient insertion on\np. 259, and are therefore appended here.\n\nThe 'random' character of male and female births has generally been\nrested almost entirely on statistics of place and time. But what is\nmore wanted, surely, is the proportion displayed when we compare a\nnumber of _families_. This seems so obvious that I cannot but suppose\nthat the investigation must have been already made somewhere, though I\nhave not found any trace of it in the most likely quarters. Thus\nProf. Lexis (_Massenerscheinungen_) when supporting his view that the\nproportion between the sexes at birth is almost the only instance\nknown to him, in natural phenomena, of true normal dispersion about a\nmean, rests his conclusions on the ordinary statistics of the\nregisters of different countries.\n\nIt certainly needs proof that the same characteristics will hold good\nwhen the family is taken as the unit, especially as some theories (e.g. that\nof Sadler) would imply that 'runs' of boys or girls would be proportionally\ncommoner than pure chance would assign. Lexis has shown that this is\nmost markedly the case with _twins_: i.e., to use an obviously intelligible\nnotation, (M for male, F for female), that M.M. and F.F. are very much\ncommoner in proportion than M.F.\n\nI have collected statistics including over 13,000 male and female\nbirths, arranged in families of four and upwards. They were taken from\nthe pedigrees in the Herald's Visitations, and therefore represent as\na rule a somewhat select class, viz. the families of the eldest sons\nof English country gentlemen in the sixteenth century. They are not\nsufficiently extensive yet for publication, but I give a summary of\nthe results to indicate their tendency so far. The upper line of\nfigures in each case gives the _observed_ results: i.e. in the case\nof a family of four, the numbers which had four male, three male and\none female, two male and two female, and so on. The lower line gives\nthe _calculated_ results; i.e. the corresponding numbers which would\nhave been obtained had batches of M.s and F.s been drawn from a bag in\nwhich they were mixed in the ratio assigned by the total observed\nnumbers for those families.\n\n512 families of 4; | m^4   m^3 f   m^2 f^2   mf^3   f^4\nyielding           |  81 +  148  +   161   +  98  +  24  (observed.)\n1188 M. : 860 F.   |  57 +  168  +   184   +  88  +  15  (calculated.)\n\n512 families of 5; | m^5   m^4 f   m^3 f^2   m^2 f^3   mf^4   f^5\nyielding           |  50 +   82  +   161   +   143   +  61  +  15  (obs.)\n1402 M. : 1158 F.  |  25 +  103  +   172   +   143   +  59  +  10  (calc.)\n\n512 families of 6; | m^6   m^5 f   m^4 f^2   m^3 f^3   m^2 f^4   mf^5   f^6\nyielding           |  30 +   48  +   115   +   146   +   126   +  40  +  7  (obs.)\n1612 M. : 1460 F.  |  10 +   56  +   133   +   159   +   108   +  41  +  5  (calc.)\n\nThe numbers for the larger families are as yet too small to be worth\ngiving, but they show the same tendency. It will be seen that in every case\nthe observed central values are less than the calculated; and that the\nobserved extreme values are much greater than the calculated. The results\nseem to suggest (so far) that a family cannot be likened to a chance drawing\nof the requisite number from _one_ bag. A better analogy would be to suppose\ntwo bags, one with M.s in excess and the other with F.s in less excess, and\nthat some persons draw from one and some from the other. But fuller\nstatistics are needed.\n\nIt will be observed that the total excess of male births is large. This\n_may_ arise from undue omission of females; but I have carefully confined\nmyself to the two or three last generations, in each pedigree, for greater\nsecurity.\n\n\n1. _Essay on Probabilities_, p. 114.\n\n2. Doubts have been expressed about the truly random character of the\n  digits in this case (v. De Morgan, _Budget of Paradoxes_, p. 291),\n  and Jevons has gone so far as to ask (_Principles of Science_,\n  p. 529), \"Why should the value of \u03c0, when expressed to a great\n  number of figures, contain the digit 7 much less frequently than any\n  other digit!\"  I do not quite understand what this means. If such a\n  question were asked in relation to any unusual divergence from the\n  _\u00e0 priori_ chance in a case of throwing dice, say, we should\n  probably substitute for it the following, as being more appropriate\n  to our science:--Assign the degree of improbability of the event in\n  question; i.e. its statistical rarity. And we should then proceed\n  to judge, in the way indicated in the text, whether this\n  improbability gave rise to any grounds of suspicion.\n\n  The calculation is simple. The actual number of 7's, in the 708\n  digits, is 53: whilst the fair average would be 71. The question is,\n  What is the chance of such a departure from the average in 708\n  turns?  By the usual methods of calculation (v. Galloway on\n  _Probability_) the chances against an excess or defect of 18 are\n  about 44 : 1, in respect of any specified digit. But of course what\n  we want to decide are the chances against _some one of the ten_\n  showing this divergence. This I estimate as being approximately\n  determined by the fraction (44/45)^{10}, viz. 0.8. This represents\n  odds of only about 4 : 1 against such an occurrence, which is\n  nothing remarkable. As a matter of fact several digits in the two\n  other magnitudes which Mr Shanks had calculated to the same length,\n  viz. Tan^{-1} 1/5 and Tan^{-1} 1/239, show the same divergencies\n  (v. _Proc. Roy. Soc._ xxi. 319).\n\n  I may call attention here to a point which should have been noticed\n  in the chapter on Randomness. We must be cautious when we decide\n  upon the random character by mere inspection. It is very instructive\n  here to compare the digits in \u03c0 with those within the 'period' of a\n  circulating decimal of very long period. That of 1 \u00f7 7699, which\n  yields the full period of 7698 figures, was calculated some years\n  ago by two Cambridge graduates (Mr Lunn and Mr Suffield), and\n  privately printed. If we confine our examination to a portion of the\n  succession the random character seems plausible; i.e. the digits,\n  and their various combinations, come out in nearly, but not exactly,\n  equal numbers. So if we take batches of 10; the averages hover\n  nicely about 45. But if we took the whole period which\n  'circulates,' we should find these characteristics overdone, and the\n  random character would disappear. That is, instead of a merely\n  ultimate approximation to equality we should have (as far as this is\n  possible) an absolute attainment of it.\n\n3. Of course this conventional estimate is nothing different in kind\n  from that which may attach to _any_ order or succession. Ten heads\n  in succession is intrinsically or objectively indistinguishable in\n  character from alternate heads and tails, or seven heads and three\n  tails, &c. Its distinction only consists in its almost universal\n  acceptance as remarkable.\n\n4. _Our Inheritance in the Great Pyramid_, Ed. III. 1877.\n\n5. Made in _Nature_ (Jan. 24, 1878) by Mr J. G. Jackson. It must be\n  remarked that Mr Smyth's alternative statement of his case leads up\n  to that explanation:--\"The vertical height of the great pyramid is\n  the radius of a theoretical circle the length of whose curved\n  circumference is exactly equal to the sum of the lengths of the four\n  straight sides of the actual and practical square base.\" As regards\n  the alternatives of chance and design, here, it must be remembered\n  in justice to Mr Smyth's argument that the antithesis he admits to\n  chance is not human, but divine design.\n\n6. See Cournot, _Essai sur les fondements de nos connaissances_.\n  Vol. I. p. 71.\n\n7. It deserves notice that considerations of this kind have found\n  their way into the Law Courts though of course without any attempt\n  at numerical valuation. Thus, in the celebrated De Ros trial, in so\n  far as the evidence was indirect, one main ground of suspicion seems\n  to have been that Lord De Ros, when dealing at whist, obtained far\n  more court cards than chance could be expected to assign him; and\n  that in consequence his average gains for several years in\n  succession were unusually large. The counsel for the defence urged\n  that still larger gains had been secured by other players without\n  suspicion of unfairness,--(I cannot find that it was explained over\n  how large an area of experience these instances had been sought; nor\n  how far the magnitude of the stakes, as distinguished from the\n  number of successes, accounted for that of the actual gains),--and\n  that large allowance must be made for skill where the actual gains\n  were computed. (See the _Times_' report, Feb. 11, 1837.)\n\n8. _Metretike_. At the end of this volume will be found a useful list\n  of a number of other publications by the same author on allied\n  topics.\n\n9. That is, if we look simply to statistical results, as Arbuthnott\n  did, and as we should do if we were examining the tosses of a\n  penny. If the remarkable theory of Dr D\u00fcsing (_Die Regulierung des\n  Geschlechts-verh\u00e4ltnisses..._ Jena, 1884) be confirmed, the matter\n  would assume a somewhat different aspect. He attempts to show, both\n  on physiological grounds, and by analysis of statistics referring to\n  men and animals, that there is a decidedly _compensatory_ process at\n  work. That is, if for any cause either sex attains a preponderance,\n  agencies are at once set in motion which tend to redress the\n  balance. This is a modification and improvement of the older theory,\n  that the relative age of the parents has something to do with the\n  sex of the offspring.\n\n  Quetelet (_Letters_, p. 61) has attempted to _prove_ a proposition\n  about the succession of male and female births by certain\n  experiments supposed to be tried upon an urn with black and white\n  balls in it. But this is going too far. (See the note at the end of\n  this chapter.)\n\n10. It is precisely analogous to the conclusion that the _flowers_ of\n  the daisies (as distinguished from the _plants_, v. p. 109) are not\n  distributed at random, but have a tendency to go in groups of two or\n  more. Mere observation shows this: and then, from our knowledge of\n  the growth of plants we may infer that these little groups spring\n  from the same root.\n\n11. In this discussion, writers often speak of the probability of a\n  \"_physical connection_\" between these double stars. The phrase seems\n  misleading, for on the usual hypothesis of universal gravitation\n  _all_ stars are physically connected, by gravitation. It is\n  therefore better, as above, to make it simply a question of relative\n  proximity, and to leave it to astronomy to infer what follows from\n  unusual proximity.\n\n12. Professor Forbes in the paper in the Philosophical Magazine\n  already referred to (Ch. VII. \u00a718) gave several diagrams to show\n  what were the actual arrangements of a random distribution. He\n  scattered peas over a chess-board, and then counted the number which\n  rested on each square. His figures seem to show that the general\n  appearance of the stars is much the same as that produced by such a\n  plan of scattering.\n\n  Some recent investigations by Mr R. A. Proctor seem to show,\n  however, that there are at least two exceptions to this tolerably\n  uniform distribution. (1) He has ascertained that the stars are\n  decidedly more thickly aggregated in the Milky Way than\n  elsewhere. So far as this is to be relied on the argument is the\n  same as in the case of the double stars; it tends to prove that the\n  proximity of the stars in the Milky Way is not merely apparent, but\n  actual. (2) He has ascertained that there are two large areas, in\n  the North and South hemispheres, in which the stars are much more\n  thickly aggregated than elsewhere. Here, it seems to me,\n  Probability proves nothing: we are simply denying that the\n  distribution is uniform. What may follow in the way of inferences\n  as to the physical process of causation by which the stars have been\n  disposed is a question for the Astronomer. See Mr Proctor's _Essays\n  on Astronomy_, p. 297. Also a series of Essays in _The Universe and\n  the coming Transits_.\n\n\n\n\nCHAPTER XI.\n\n\n_ON CERTAIN CONSEQUENCES OF THE OBJECTIVE TREATMENT OF A SCIENCE OF\nINFERENCE._[1]\n\n1. In the previous edition a large part of this chapter was devoted to\n  the general consideration of the distinction between a Material and\n  a Conceptualist view of Logic. I have omitted most of this here, as\n  also a large part of a chapter devoted to the detailed discussion of\n  the Law of Causation, as I hope before very long to express my\n  opinions on these subjects more fully, and more appropriately, in a\n  treatise on the general principles of Inductive Logic.\n\n\n1. Students of Logic are familiar with that broad\ndistinction between the two methods of treatment to which\nthe names of Material and Conceptualist may be applied.\nThe distinction was one which had been gradually growing\nup under other names before it was emphasized, and treated\nas a distinction within the field of Logic proper, by the publication\nof Mill's well known work. No one, for instance,\ncan read Whewell's treatises on Induction, or Herschel's\nDiscourse, without seeing that they are treating of much the\nsame subject-matter, and regarding it in much the same\nway, as that which Mill discussed under the name of Logic,\nthough they were not disposed to give it that name. That\nis, these writers throughout took it for granted that what\nthey had to do was to systematise the facts of nature in\ntheir objective form, and under their widest possible treatment,\nand to expound the principal modes of inference and\nthe principal practical aids in the investigation of these\nmodes of inference, which reason could suggest and which\nexperience could justify. What Mill did was to bring these\nmethods into close relation with such portions of the old\nscholastic Logic as he felt able to retain, to work them out\ninto much fuller detail, to systematize them by giving them\na certain philosophical and psychological foundation,--and\nto entitle the result _Logic_.\n\nThe practical treatment of a science will seldom correspond\nclosely to the ideal which its supporters propose to\nthemselves, and still seldomer to that which its antagonists\ninsist upon demanding from the supporters. If we were to\ntake our account of the distinction between the two views of\nLogic expounded respectively by Hamilton and by Mill,\nfrom Mill and Hamilton respectively, we should certainly\nnot find it easy to bring them under one common definition.\nBy such a test, the material Logic would be regarded as\nnothing more than a somewhat arbitrary selection from the\ndomain of Physical Science in general, and the conceptualist\nLogic nothing more than a somewhat arbitrary selection from\nthe domain of Psychology. The former would omit all consideration\nof the laws of thought and the latter all consideration\nof the truth or falsehood of our conclusions.\n\nOf course, in practice, such extremes as these are soon\nseen to be avoidable, and in spite of all controversial exaggerations\nthe expounders of the opposite views do contrive to\nretain a large area of speculation in common. I do not propose\nhere to examine in detail the restrictions by which this\naccommodation is brought about, or the very real and important\ndistinctions of method, aim, tests, and limits which\nin spite of all approach to agreement are still found to subsist.\nTo attempt this would be to open up rather too wide an\nenquiry to be suitable in a treatise on one subdivision only\nof the general science of Inference.\n\n2. One subdivision of this enquiry is however really\nforced upon our notice. It does become important to consider\nthe restrictions to which the ultra-material account of\nthe province of Logic has to be subjected, because we shall\nthus have our attention drawn to an aspect of the subject\nwhich, slight and fleeting as it is within the region of Induction\nbecomes very prominent and comparatively permanent\nin that of Probability. According to this ultra-material view,\nInductive Logic would generally be considered to have nothing\nto do with anything but objective facts: its duty is to\nstart from facts and to confine itself to such methods as will\nyield nothing but facts. What is doubtful it either establishes\nor it lets alone for the present, what is unattainable\nit rejects, and in this way it proceeds to build up by slow\naccretion a vast fabric of certain knowledge.\n\nBut of course all this is supposed to be done by human\nminds, and therefore if we enquire whether notions or concepts,--call\nthem what we will,--have no place in such a\nscheme it must necessarily be admitted that they _have_ some\nplace. The facts which form our starting point must be\ngrasped by an intelligent being before inference can be built\nupon them; and the 'facts' which form the conclusion have\noften, at any rate for some time, no place anywhere else than\nin the mind of man. But no one can read Mill's treatise, for\ninstance, without noticing how slight is his reference to this\naspect of the question. He remarks, in almost contemptuous\nindifference, that the man who digs must of course have a\nnotion of the ground he digs and of the spade he puts into\nit, but he evidently considers that these 'notions' need not\nmuch more occupy the attention of the speculative logician,\nin so far as his mere inferences are concerned, than they\noccupy that of the husbandman.\n\n3. It must be admitted that there is some warrant\nfor this omission of all reference to the subjective side of\ninference so long as we are dealing with Inductive Logic.\nThe inductive _discoverer_ is of course in a very different\nposition. If he is worthy of the name his mind at every\nmoment will be teeming with notions which he would be as\nfar as any one from calling facts: he is busy making them\nsuch to the best of his power. But the logician who follows\nin his steps, and whose business it is to explain and justify\nwhat his leader has discovered, is rather apt to overlook this\nmental or uncertain stage. What he mostly deals in are the\n'complete inductions' and 'well-grounded generalizations'\nand so forth, or the exploded errors which contradict them:\nthe prisoners and the corpses respectively, which the real\ndiscoverer leaves on the field behind him whilst he presses\non to complete his victory. The whole method of science,--expository\nas contrasted with militant,--is to emphasize the\ndistinction between fact and non-fact, and to treat of little\nelse but these two. In other words a treatise on Inductive\nLogic _can_ be written without any occasion being found to\ndefine what is meant by a notion or concept, or even to employ\nsuch terms.\n\n4. And yet, when we come to look more closely, signs\nmay be detected even within the field of Inductive Logic,\nof an occasional breaking down of the sharp distinction in\nquestion; we may meet now and then with entities (to use\nthe widest term attainable) in reference to which it would\nbe hard to say that they are either facts or conceptions.\nFor instance, Inductive Logic has often occasion to make use\nof Hypotheses: to which of the above two classes are these\nto be referred? They do not seem in strictness to belong to\neither; nor are they, as will presently be pointed out, by any\nmeans a solitary instance of the kind.\n\nIt is true that within the province of Inductive Logic\nthese hypotheses do not give much trouble on this score.\nHowever vague may be the form in which they first present\nthemselves to the philosopher's mind, they have not much\nbusiness to come before us in our capacity of logicians until\nthey are well on their way, so to say, towards becoming\nfacts: until they are beginning to harden into that firm\ntangible shape in which they will eventually appear. We\ngenerally have some such recommendations given to us as\nthat our hypotheses shall be well-grounded and reasonable.\nThis seems only another way of telling us that however\nfreely the philosopher may make his guesses in the privacy\nof his own study, he had better not bring them out into\npublic until they can with fair propriety be termed facts,\neven though the name be given with some qualification, as\nby terming them 'probable facts.' The reason, therefore,\nwhy we do not take much account of this intermediate state\nin the hypothesis, when we are dealing with the inductive\nprocesses, is that here at any rate it plays only a temporary\npart; its appearance in that guise is but very fugitive. If\nthe hypothesis be a sound one, it will soon take its place as\nan admitted fact; if not, it will soon be rejected altogether.\nIts state as a hypothesis is not a normal one, and therefore\nwe have not much occasion to scrutinize its characteristics.\nIn so saying, it must of course be understood that we are\nspeaking as inductive logicians; the philosopher in his workshop\nought, as already remarked, to be familiar enough with\nthe hypothesis in every stage of its existence from its origin;\nbut the logician's duty is different, dealing as he does with\nproof rather than with the processes of original investigation\nand discovery.\n\nWe might indeed even go further, and say that in many\ncases the hypothesis does not present itself to the reader,\nthat is to the recipient of the knowledge, until it has ceased\nto deserve that name at all. It may be first suggested to\nhim along with the proof which establishes it, he not having\nhad occasion to think of it before. It thus comes at a single\nstep out of the obscurity of the unknown into the full possession\nof its rights as a fact, skipping practically the intermediate\nor hypothetical stage altogether. The original investigator\nhimself may have long pondered over it, and kept\nit present to his mind, in this its dubious stage, but finally\nhave given it to the world with that amount of evidence\nwhich raises it at once in the minds of others to the level of\ncommonly accepted facts.\n\nStill this doubtful stage exists in every hypothesis,\nthough for logical purposes, and to most minds, it exists\nin a very fugitive way only. When attention has been\ndirected to it, it may be also detected elsewhere in Logic.\nTake the case, for instance, of the reference of names.\nMill gives the examples of the sun, and a battle, as distinguished\nfrom the ideas of them which we, or children,\nmay entertain. Here the distinction is plain and obvious\nenough. But if, on the other hand, we take the case of\nthings whose existence is doubtful or disputed, the difficulty\nabove mentioned begins to show itself. The case of merely\nextinct things, or such as have not yet come into existence,\noffers indeed no trouble, since of course actually _present_\nexistence is not necessary to constitute a fact. The usual\ndistinction may even be retained also in the case of mythical\nexistences. Centaur and Griffin have as universally recognised\na significance amongst the poets, painters, and heralds\nas lion and leopard have. Hence we may claim, even here,\nthat our conceptions shall be 'truthful,' 'consistent with\nfact,' and so on, by which we mean that they are to be in\naccordance with universal convention upon such subjects.\nNecessary and universal accordance is sometimes claimed\nto be all that is meant by 'objective,' and since universal\naccordance is attainable in the case of the notoriously fictitious,\nour fundamental distinction between fact and conception,\nand our determination that our terms shall refer to\nwhat is objective rather than to what is subjective, may with\nsome degree of strain be still conceived to be tenable even here.\n\n5. But when we come to the case of disputed phenomena\nthe difficulty re-emerges. A supposed planet or\nnew mineral, a doubtful fact in history, a disputed theological\ndoctrine, are but a few examples out of many that might be\noffered. What some persons strenuously assert, others as\nstrenuously deny, and whatever hope there may be of speedy\nagreement in the case of physical phenomena, experience\nshows that there is not much prospect of this in the case of\nthose which are moral and historical, to say nothing of theological.\nSo long as those who are in agreement confine their\nintercourse to themselves, their 'facts' are accepted as such,\nbut as soon as they come to communicate with others all\ndistinction between fact and conception is lost at once, the\n'facts' of one party being mere groundless 'conceptions' to\ntheir opponents. There is therefore, I think, in these cases\na real difficulty in carrying out distinctly and consistently\nthe account which the Materialist logician offers as to the\nreference of names. It need hardly be pointed out that\nwhat thus applies to names or terms applies equally to\npropositions in which particular or general statements are\nmade involving names.\n\n6. But when we step into Probability, and treat this\nfrom the same material or Phenomenal point of view, we can\nno longer neglect the question which is thus presented to us.\nThe difficulty cannot here be rejected, as referring to what is\nmerely temporary or occasional. The intermediate condition\nbetween conjecture and fact, so far from being temporary\nor occasional only, is here normal. It is just the condition\nwhich is specially characteristic of Probability. Hence it\nfollows that however decidedly we may reject the Conceptualist\ntheory we cannot altogether reject the use of\nConceptualist language. If we can prove that a given man\nwill die next year, or attain sufficiently near to proof to\nleave us practically certain on the point, we may speak of\nhis death as a (future) fact. But if we merely contemplate\nhis death as probable? This is the sort of inference, or\nsubstitute for inference, with which Probability is specially\nconcerned. We may, if we so please, speak of 'probable\nfacts,' but if we examine the meaning of the words we\nmay find them not merely obscure, but self-contradictory.\nDoubtless there are facts here, in the fullest sense of the\nterm, namely the statistics upon which our opinion is ultimately\nbased, for these are known and admitted by all who\nhave looked into the matter. The same language may also\nbe applied to that extension of these statistics by induction\nwhich is involved in the assertion that similar statistics\nwill be found to prevail elsewhere, for these also may rightfully\nclaim universal acceptance. But these statements, as\nwas abundantly shown in the earlier chapters, stand on a\nvery different footing from a statement concerning the individual\nevent; the establishment and discussion of the\nformer belong by rights to Induction, and only the latter\nto Probability.\n\n7. It is true that for want of appropriate terms to\nexpress such things we are often induced, indeed compelled,\nto apply the same name of 'facts' to such individual contingencies.\nWe should not, for instance, hesitate to speak of\nthe fact of the man dying being probable, possible, unlikely,\nor whatever it might be. But I cannot help regarding such\nexpressions as a strictly incorrect usage arising out of a\ndeficiency of appropriate technical terms. It is doubtless\ncertain that one or other of the two alternatives must happen,\nbut this alternative certainty is not the subject of our contemplation;\nwhat we have before us is the _single_ alternative,\nwhich is notoriously uncertain. It is this, and this only,\nwhich is at present under notice, and whose occurrence has\nto be estimated. We have surely no right to dignify this\nwith the name of a fact, under any qualifications, when the\nopposite alternative has claims, not perhaps actually equal to,\nbut at any rate not much inferior to its own. Such language,\nas already remarked, may be quite right in Inductive logic,\nwhere we are only concerned with conjectures of such a high\ndegree of likelihood that their non-occurrence need not be\ntaken into practical account, and which are moreover regarded\nas merely temporary. But in Probability the conjecture\nmay have any degree of likelihood about it; it may be just\nas likely as the other alternative, nay it may be much less\nlikely. In these latter cases, for instance, if the chances are\nvery much against the man's death, it is surely an abuse of\nlanguage to speak of the 'fact' of his dying, even though we\nqualify it by declaring it to be highly improbable. The\nsubject-matter essential to Probability being the uncertain,\nwe can never with propriety employ upon it language which\nin its original and correct application is only appropriate to\nwhat is actually or approximately certain.\n\n8. It should be remembered also that this state of\nthings, thus characteristic of Probability, is _permanent_ there.\nSo long as they remain under the treatment of that science\nour conjectures, or whatever we like to call them, never\ndevelop into facts. I calculate, for instance, the chance that\na die will give ace, or that a man will live beyond a certain\nage. Such an approximation to knowledge as is thus acquired\nis as much as we can ever afterwards hope to get,\nunless we resort to other methods of enquiry. We do not, as\nin Induction, feel ourselves on the brink of some experimental\nor other proof which at any moment may raise it\ninto certainty. It is nothing but a conjecture of a certain\ndegree of strength, and such it will ever remain, so long as\nProbability is left to deal with it. If anything more is ever\nto be made out of it we must appeal to direct experience, or\nto some kind of inductive proof. As we have so often said,\nindividual facts can never be determined here, but merely\nultimate tendencies and averages of many events. I may,\nindeed, by a second appeal to Probability improve the\ncharacter of my conjecture, through being able to refer it to\na narrower and better class of statistics; but its essential\nnature remains throughout what it was.\n\nIt appears to me therefore that the account of the Materialist\nview of logic indicated at the commencement of this\nchapter, though substantially sound, needs some slight reconsideration\nand re-statement. It answers admirably so far as\nordinary Induction is concerned, but needs some revision\nif it is to be equally applicable to that wider view of\nthe nature and processes of acquiring knowledge wherein\nthe science of logic is considered to involve Probability\nalso as well as Induction.\n\n9. Briefly then it is this. We regard the scientific\nthinker, whether he be the original investigator who discovers,\nor the logician who analyses and describes the proofs\nthat may be offered, as surrounded by a world of objective\nphenomena extending indefinitely both ways in time, and in\nevery direction in space. Most of them are, and always will\nremain, unknown. If we speak of them as facts we mean\nthat they are potential objects of human knowledge, that\nunder appropriate circumstances men could come to determinate\nand final agreement about them. The scientific or\nmaterial logician has to superintend the process of converting\nas much as possible of these unknown phenomena into what\nare known, of aggregating them, as we have said above, about\nthe nucleus of certain data which experience and observation\nhad to start with. In so doing his principal resources are\nthe Methods of Induction, of which something has been\nsaid in a former chapter; another resource is found in the\nTheory of Probability, and another in Deduction.\n\nNow, however such language may be objected to as\nsavouring of Conceptualism, I can see no better compendious\nway of describing these processes than by saying that we are\nengaged in getting at conceptions of these external phenomena,\nand as far as possible converting these conceptions\ninto facts. What is the natural history of 'facts' if we trace\nthem back to their origin? They first come into being as\nmere guesses or conjectures, as contemplated possibilities\nwhose correspondence with reality is either altogether disbelieved\nor regarded as entirely doubtful. In this stage, of\ncourse, their contrast with facts is sharp enough. _How_ they\narise it does not belong to Logic but to Psychology to say.\nLogic indeed has little or nothing to do with them whilst\nthey are in this form. Everyone is busy all his life in entertaining\nsuch guesses upon various subjects, the superiority of\nthe philosopher over the common man being mainly found in\nthe quality of his guesses, and in the skill and persistence\nwith which he sifts and examines them. In the next stage\nthey mostly go by the name of theories or hypotheses, when\nthey are comprehensive in their scope, or are in any way on\na scale of grandeur and importance: when however they are\nof a trivial kind, or refer to details, we really have no distinctive\nor appropriate name for them, and must be content\ntherefore to call them 'conceptions.' Through this stage\nthey flit with great rapidity in Inductive Logic; often the\nlogician keeps them back until their evidence is so strong\nthat they come before the world at once in the full dignity\nof facts. Hence, as already remarked, this stage of their\ncareer is not much dwelt upon in Logic. But the whole\nbusiness of Probability is to discuss and estimate them at\nthis point. Consequently, so far as this science is concerned,\nthe explanation of the Material logician as to the reference\nof names and propositions has to be modified.\n\n10. The best way therefore of describing our position\nin Probability is as follows:--We are _entertaining a conception_\nof some event, past, present, or future. From the nature\nof the case this conception is all that can be actually entertained\nby the mind. In its present condition it would be\nincorrect to call it a fact, though we would willingly, if we\ncould, convert it into such by making certain of it one way\nor the other. But so long as our conclusions are to be\neffected by considerations of Probability only, we cannot do\nthis. The utmost we can do is to _estimate_ or _evaluate_ it.\nThe whole function of Probability is to give rules for so\ndoing. By means of reference to statistics or by direct\ndeduction, as the case may be, we are enabled to say how\nmuch this conception is to be believed, that is in what proportion\nout of the total number of cases we shall be right\nin so doing. Our position, therefore, in these cases seems\ndistinctly that of entertaining a conception, and the process\nof inference is that of ascertaining to what extent we are\njustified in adding this conception to the already received\nbody of truth and fact.\n\nSo long, then, as we are confined to Probability these\nconceptions remain such. But if we turn to Induction we\nsee that they are meant to go a step further. Their final\nstage is not reached until they have ripened into facts, and\nso taken their place amongst uncontested truths. This is\ntheir final destination in Logic, and our task is not accomplished\nuntil they have reached it.\n\n11. Such language as this in which we speak of our\nposition in Probability as being that of entertaining a conception,\nand being occupied in determining what degree of\nbelief is to be assigned to it, may savour of Conceptualism,\nbut is in spirit perfectly different from it. Our ultimate\nreference is always to facts. We start from them as our data,\nand reach them again eventually in our results whenever it\nis possible. In Probability, of course, we cannot do this in\nthe individual result, but even then (as shown in Ch. VI.) we\nalways _justify_ our conclusions by appeal to facts, viz. to what\nhappens in the long run.\n\nThe discussion which has been thus given to this part of\nthe subject may seem somewhat tedious, but it was so obviously\nforced upon us when considering the distinction\nbetween the two main views of Logic, that it was impossible\nto pass it over without fear of misapprehension and confusion.\nMoreover, as will be seen in the course of the next\nchapter, several important conclusions could not have been\nproperly explained and justified without first taking pains\nto make this part of our ground perfectly plain and satisfactory.\n\n\n\n\n\n\nCHAPTER XII.\n\n\n_CONSEQUENCES OF THE FOREGOING DISTINCTIONS._\n\n1. We are now in a position to explain and justify some\nimportant conclusions which, if not direct consequences of\nthe distinctions laid down in the last chapter, will at any\nrate be more readily appreciated and accepted after that\nexposition.\n\nIn the first place, it will be seen that in Probability _time_\nhas nothing to do with the question; in other words, it does\nnot matter whether the event, whose probability we are discussing,\nbe past, present, or future. The problem before us,\nin its simplest form, is this:--Statistics (extended by Induction,\nand practically often gained by Deduction) inform us\nthat a certain event has happened, does happen, or will\nhappen, in a certain way in a certain proportion of cases.\nWe form a conception of that event, and regard it as possible;\nbut we want to do more; we want to know _how much_ we\nought to expect it (under the explanations given in a former\nchapter about quantity of belief). There is therefore a\nsort of relative futurity about the event, inasmuch as our\nknowledge of the fact, and therefore our justification or\notherwise of the correctness of our surmise, almost necessarily\ncomes after the surmise was formed; but the futurity\nis only relative. The evidence by which the question is to\nbe settled may not be forthcoming yet, or we may have it by\nus but only consult it afterwards. It is from the fact of the\nfuturity being, as above described, only relative, that I have\npreferred to speak of the conception of the event rather than\nof the anticipation of it. The latter term, which in some respects\nwould have seemed more intelligible and appropriate,\nis open to the objection, that it does rather, in popular estimation,\nconvey the notion of an absolute as opposed to a\nrelative futurity.\n\n2. For example; a die is thrown. Once in six times\nit gives ace; if therefore we assume, without examination,\nthat the throw is ace, we shall be right once in six times.\nIn so doing we may, according to the usual plan, go _forwards_\nin time; that is, form our opinion about the throw beforehand,\nwhen no one can tell what it will be. Or we might go\n_backwards_; that is, form an opinion about dice that had\nbeen cast on some occasion in time past, and then correct\nour opinion by the testimony of some one who had been a\nwitness of the throws. In either case the mental operation\nis precisely the same; an opinion formed merely on statistical\ngrounds is afterwards corrected by specific evidence. The\nopinion may have been formed upon a past, present, or future\nevent; the evidence which corrects it afterwards may be our\nown eyesight, or the testimony of others, or any kind of inference;\nby the evidence is merely meant such subsequent\nexamination of the case as is assumed to set the matter at\nrest. It is quite possible, of course, that this specific evidence\nshould never be forthcoming; the conception in that\ncase remains as a conception, and never obtains that degree\nof conviction which qualifies it to be regarded as a 'fact.'\nThis is clearly the case with all past throws of dice the results\nof which do not happen to have been recorded.\n\nIn discussing games of chance there are obvious advantages\nin confining ourselves to what is really, as well as\nrelatively, future, for in that case direct information concerning\nthe contemplated result being impossible, all persons are\non precisely the same footing of comparative ignorance, and\nmust form their opinion entirely from the known or inferred\nfrequency of occurrence of the event in question. On the\nother hand, if the event be passed, there is almost always evidence\nof some kind and of some value, however slight, to\ninform us what the event really was; if this evidence is not\nactually at hand, we can generally, by waiting a little, obtain\nsomething that shall be at least of some use to us in forming\nour opinion. Practically therefore we generally confine ourselves,\nin anticipations of this kind, to what is really future,\nand so in popular estimation futurity becomes indissolubly\nassociated with probability.\n\n3. There is however an error closely connected with\nthe above view of the subject, or at least an inaccuracy of\nexpression which is constantly liable to lead to error, which\nhas found wide acceptance, and has been sanctioned by\nwriters of the greatest authority. For instance, both Butler,\nin his _Analogy_, and Mill, have drawn attention, under one\nform of expression or another, to the distinction between improbability\nbefore the event and improbability after the\nevent, which they consider to be perfectly different things.\nThat this phraseology indicates a distinction of importance\ncannot be denied, but it seems to me that the language in\nwhich it is often expressed requires to be amended.\n\nButler's remarks on this subject occur in his _Analogy_, in\nthe chapter on miracles. Admitting that there is a strong\npresumption against miracles (his equivalent for the ordinary\nexpression, an 'improbability before the event') he\nstrives to obtain assent for them by showing that other\nevents, which also have a strong presumption against them,\nare received on what is in reality very slight evidence. He\nsays, \"There is a very strong presumption against common\nspeculative truths, and against the most ordinary facts, before\nthe proof of them; which yet is overcome by almost any\nproof. There is a presumption of millions to one against the\nstory of C\u00e6sar, or of any other man. For, suppose a number\nof common facts so and so circumstanced, of which one had\nno kind of proof, should happen to come into one's thoughts,\nevery one would without any possible doubt conclude them\nto be false. And the like may be said of a single common\nfact.\"\n\n4. These remarks have been a good deal criticized,\nand they certainly seem to me misleading and obscure in\ntheir reference. If one may judge by the context, and by\nanother passage in which the same argument is afterwards\nreferred to,[1] it would certainly appear that Butler drew no\ndistinction between miraculous accounts, and other accounts\nwhich, to use any of the various expressions in common use,\nare unlikely or improbable or have a presumption against\nthem; and concluded that since some of the latter were instantly\naccepted upon somewhat mediocre testimony, it was\naltogether irrational to reject the former when similarly or\nbetter supported.[2] This subject will come again under our\nnotice, and demand fuller discussion, in the chapter on the\nCredibility of extraordinary stories. It will suffice here to\nremark that, however satisfactory such a view of the matter\nmight be to some theologians, no antagonist of miracles\nwould for a moment accept it. He would naturally object\nthat, instead of the miraculous element being (as Butler\nconsiders) \"a small additional presumption\" against the\nnarrative, it involved the events in a totally distinct class of\nincredibility; that it multiplied, rather than merely added\nto, the difficulties and objections in the way of accepting\nthe account.\n\nMill's remarks (_Logic_, Bk. III. ch. XXV. \u00a74) are of a different\ncharacter. Discussing the grounds of disbelief he\nspeaks of people making the mistake of \"overlooking the\ndistinction between (what may be called) improbability\nbefore the fact, and improbability after it, two different\nproperties, the latter of which is always a ground of disbelief,\nthe former not always.\" He instances the throwing\nof a die. It is improbable beforehand that it should turn\nup ace, and yet afterwards, \"there is no reason for disbelieving\nit if any credible witness asserts it.\" So again, \"the\nchances are greatly against A. B.'s dying, yet if any one tells\nus that he died yesterday we believe it.\"\n\n5. That there is some difficulty about such problems\nas these must be admitted. The fact that so many people\nfind them a source of perplexity, and that such various\nexplanations are offered to solve the perplexity, are a sufficient\nproof of this.[3] The considerations of the last chapter,\nhowever, over-technical and even scholastic as some of the\nlanguage in which it was expressed may have seemed to the\nreader, will I hope guide us to a more satisfactory way of\nregarding the matter.\n\nWhen we speak of an improbable event, it must be\nremembered that, objectively considered, an event can only\nbe more or less _rare_; the extreme degree of rarity being of\ncourse that in which the event does not occur at all. Now,\nas was shown in the last chapter, our position, when forming\njudgments of the time in question, is that of entertaining\na conception or conjecture (call it what we will), and assigning\na certain weight of trustworthiness to it. The real\ndistinction, therefore, between the two classes of examples\nrespectively, which are adduced both by Butler and by Mill,\nconsists in the way in which those conceptions are obtained;\nthey being obtained in one case by the process of guessing,\nand in the other by that of giving heed to the reports of\nwitnesses.\n\n6. Take Butler's instance first. In the 'presumption\nbefore the proof' we have represented to us a man thinking\nof the story of C\u00e6sar, that is, making a guess about certain\nhistorical events without any definite grounds for it, and\nthen speculating as to what value is to be attached to the\nprobability of its truth. Such a guess is of course, as he\nsays, concluded to be false. But what does he understand\nby the 'presumption after the proof'? That a story not\nadopted at random, but actually suggested and supported by\nwitnesses, should be true. The latter might be accepted,\nwhilst the former would undoubtedly be rejected; but all\nthat this proves, or rather illustrates, is that the testimony\nof almost any witness is in most cases vastly better than\na mere guess.[4] We may in both cases alike speak of 'the\nevent' if we will; in fact, as was admitted in the last\nchapter, common language will not readily lend itself to any\nother way of speaking. But it should be clearly understood\nthat, phrase it how we will, what is really present to\nthe man's mind, and what is to have its probable value\nassigned to it, is the conception of an event, in the sense in\nwhich that expression has already been explained. And\nsurely no two conceptions can have a much more important\ndistinction put between them than that which is involved in\nsupposing one to rest on a mere guess, and the other on the\nreport of a witness. Precisely the same remarks apply to\nthe example given by Mill. Before A. B.'s death our\nopinion upon the subject was nothing but a guess of our\nown founded upon life statistics; after his death it was\nfounded upon the evidence of some one who presumably\nhad tolerable opportunities of knowing what the facts really\nwere.\n\n7. That the distinction before us has no essential connection\nwhatever with time is indeed obvious on a moment's\nconsideration. Conceive for a moment that some one had\nopportunities of knowing whether A. B. would die or not.\nIf he told us that A. B. would die to-morrow, we should in\nthat case be just as ready to believe him as when he tells us\nthat A. B. _has_ died. If we continued to feel any doubt\nabout the statement (supposing always that we had full\nconfidence about his veracity in matters into which he had\nduly enquired), it would be because we thought that in his\ncase, as in ours, it was equivalent to a guess, and nothing\nmore. So with the event when past, the fact of its being\npast makes no difference whatever; until the credible witness\ninforms us of what he knows to have occurred, we\nshould doubt it if it happened to come into our minds, just\nas much as if it were future.\n\nThe distinction, therefore, between probability before the\nevent and probability after the event seems to resolve itself\nsimply into this;--before the event we often have no better\nmeans of information than to appeal to statistics in some\nform or other, and so to guess amongst the various possible\nalternatives; after the event the guess may most commonly\nbe improved or superseded by appeal to specific evidence,\nin the shape of testimony or observation. Hence, naturally,\nour estimate in the latter case is commonly of much more\nvalue. But if these characteristics were anyhow inverted;\nif, that is, we were to confine ourselves to guessing about the\npast, and if we could find any additional evidence about the\nfuture, the respective values of the different estimates would\nalso be inverted. The difference between these values has\nno necessary connection with time, but depends entirely\nupon the different grounds upon which our conception or\nconjecture about the event in question rests.\n\n8. The following imaginary example will serve to\nbring out the point indicated above. Conceive a people with\nvery short memories, and who preserved no kind of record to\nperpetuate their hold upon the events which happened\namongst them.[5] The whole region of the past would then be\nto them what much of the future is to us; viz. a region of\nguesses and conjectures, one in reference to which they\ncould only judge upon general considerations of probability,\nrather than by direct and specific evidence. But conceive\nalso that they had amongst them a race of prophets who\ncould succeed in foretelling the future with as near an\napproach to accuracy and trustworthiness as our various\nhistories, and biographies, and recollections, can attain in\nrespect to the past. The present and usual functions of\ndirect evidence or testimony, and of probability, would then\nbe simply inverted; and so in consequence would the present\naccidental characteristics of improbability before and\nafter the event. It would then be the latter which would\nby comparison be regarded as 'not always a ground of disbelief,'\nwhereas in the case of the former we should then\nhave it maintained that it always was so.\n\n9. The origin of the mistake just discussed is worth\nenquiring into. I take it to be as follows. It is often the\ncase, as above remarked, when we are speculating about\na future event, and almost always the case when that future\nevent is taken from a game of chance, that all persons are in\nprecisely the same condition of ignorance in respect to it.\nThe limit of available information is confined to statistics,\nand amounts to the knowledge that the unknown event\nmust assume some one of various alternative forms. The\nconjecture, therefore, of any one man about it is as valuable\nas that of any other. But in regard to the past the case is\nvery different. Here we are not in the habit of relying\nupon statistical information. Hence the conjectures of different\nmen are of extremely different values; in the case of\nmany they amount to what we call positive knowledge.\nThis puts a broad distinction, in popular estimation, between\nwhat may be called the objective certainty of the past and of\nthe future, a distinction, however, which from the standing-point\nof a science of inference ought to have no existence.\n\nIn consequence of this, when we apply to the past and\nthe future respectively the somewhat ambiguous expression\n'the chance of the event,' it commonly comes to bear very\ndifferent significations. Applied to the future it bears its\nproper meaning, namely, the value to be assigned to a conjecture\nupon statistical grounds. It does so, because in this\ncase hardly any one has more to judge by than such conjectures.\nBut applied to the past it shifts its meaning,\nowing to the fact that whereas some men have conjectures\nonly, others have positive knowledge. By the chance of the\nevent is now often meant, not the value to be assigned to a\nconjecture founded on statistics, but to such a conjecture\nderived from and enforced by any body else's conjecture, that\nis by his knowledge and his testimony.\n\n10. There is a class of cases in apparent opposition to\nsome of the statements in this chapter, but which will be\nfound, when examined closely, decidedly to confirm them.\nI am walking, say, in a remote part of the country, and suddenly\nmeet with a friend. At this I am naturally surprised.\nYet if the view be correct that we cannot properly speak\nabout events in themselves being probable or improbable,\nbut only say this of our conjectures about them, how do we\nexplain this? We had formed no conjecture beforehand,\nfor we were not thinking about anything of the kind, but\nyet few would fail to feel surprise at such an incident.\n\nThe reply might fairly be made that we _had_ formed\nsuch anticipations tacitly. On any such occasion every\none unconsciously divides things into those which are known\nto him and those which are not. During a considerable\nprevious period a countless number of persons had met us,\nand all fallen into the list of the unknown to us. There\nwas nothing to remind us of having formed the anticipation\nor distinction at all, until it was suddenly called out\ninto vivid consciousness by the exceptional event. The\nwords which we should instinctively use in our surprise seem\nto show this:--'Who would have thought of seeing you\nhere?' viz. Who would have given any weight to the latent\nthought if it had been called out into consciousness beforehand?\nWe put our words into the past tense, showing that\nwe have had the distinction lurking in our minds all the\ntime. We always have a multitude of such ready-made\nclasses of events in our minds, and when a thing happens to\nfall into one of those classes which are very small we cannot\nhelp noticing the fact.\n\nOr suppose I am one of a regiment into which a shot\nflies, and it strikes me, and me only. At this I am surprised,\nand why? Our common language will guide us to the\nreason. 'How strange that it should just have hit _me_ of all\nmen!' We are thinking of the very natural two-fold division\nof mankind into, ourselves, and everybody else; our surprise\nis again, as it were, retrospective, and in reference to this\ndivision. No anticipation was distinctly formed, because\nwe did not think beforehand of the event, but the event,\nwhen it has happened, is at once assigned to its appropriate\nclass.\n\n11. This view is confirmed by the following considerations.\nTell the story to a friend, and he will be a little\nsurprised, but less so than we were, _his_ division in this\nparticular case being,--his friends (of whom we are but one),\nand the rest of mankind. It is not a necessary division, but\nit is the one which will be most likely suggested to him.\n\nTell it again to a perfect stranger, and his division being\ndifferent (viz. we falling into the majority) we shall fail to\nmake him perceive that there is anything at all remarkable\nin the event.\n\nIt is not of course attempted in these remarks to justify\nour surprise in every case in which it exists. Different\npersons might be differently affected in the cases supposed,\nand the examples are therefore given mainly for illustration.\nStill on principles already discussed (Ch. VI. \u00a732) we might\nexpect to find something like a general justification of the\namount of surprise.\n\n12. The answer commonly given in these cases is\nconfined to attempting to show that the surprise should not\narise, rather than to explaining how it does arise. It takes\nthe following form,--'You have no right to be surprised, for\nnothing remarkable has really occurred. If this particular\nthing had not happened something equally improbable\nmust. If the shot had not hit you or your friend, it must\nhave hit some one else who was _\u00e0 priori_ as unlikely to be\nhit.'\n\nFor one thing this answer does not explain the fact\nthat almost every one _is_ surprised in such cases, and surprised\nsomewhat in the different proportions mentioned\nabove. Moreover it has the inherent unsatisfactoriness\nof admitting that something improbable has really happened,\nbut getting over the difficulty by saying that all the\nother alternatives were equally improbable. A natural inference\nfrom this is that there is a class of things, in themselves\nreally improbable, which can yet be established upon\nvery slight evidence. Butler accepted this inference, and\nworked it out to the strange conclusion given above. Mill\nattempts to avoid it by the consideration of the very different\nvalues to be assigned to improbability before and after\nthe event. Some further discussion of this point will be\nfound in the chapter on Fallacies, and in that on the Credibility\nof Extraordinary Stories.\n\n13. In connection with the subject at present under\ndiscussion we will now take notice of a distinction which we\nshall often find insisted on in works on Probability, but to\nwhich apparently needless importance has been attached.\nIt is frequently said that probability is _relative_, in the sense\nthat it has a different value to different persons according\nto their respective information upon the subject in question.\nFor example, two persons, A and B, are going to draw\na ball from a bag containing 4 balls: A knows that the\nballs are black and white, but does not know more;\nB knows that three are black and one white. It would\nbe said that the probability of a white ball to A is 1/2, and\nto B 1/4.\n\nWhen however we regard the subject from the material\nstanding point, there really does not seem to me much more\nin this than the principle, equally true in every other science,\nthat our inferences will vary according to the data we assume.\nWe might on logical grounds with almost equal\npropriety speak of the area of a field or the height of a\nmountain being relative, and therefore having one value to\none person and another to another. The real meaning of the\nexample cited above is this: A supposes that he is choosing\nwhite at random out of a series which in the long run would\ngive white and black equally often; B supposes that he\nis choosing white out of a series which in the long run would\ngive three black to one white. By the application, therefore,\nof a precisely similar rule they draw different conclusions;\nbut so they would under the same circumstances in\nany other science. If two men are measuring the height of\na mountain, and one supposes his base to be 1000 feet,\nwhilst the other takes it to be 1001, they would of course\nform different opinions about the height. The science of\nmensuration is not supposed to have anything to do with\nthe truth of the data, but assumes them to have been correctly\ntaken; why should not this be equally the case with\nProbability, making of course due allowance for the peculiar\ncharacter of the data with which it is concerned?\n\n14. This view of the relativeness of probability is\nconnected, as it appears to me, with the subjective view of\nthe science, and is indeed characteristic of it. It seems a\nfair illustration of the weak side of that view, that it should\nlead us to lay any stress on such an expression. As was\nfully explained in the last chapter, in proportion as we work\nout the Conceptualist principle we are led away from the\nfundamental question of the material logic, viz. Is our belief\nactually correct, or not? and, if the former, to what extent\nand degree is it correct? We are directed rather to ask,\nWhat belief does any one as a matter of fact hold? And,\nsince the belief thus entertained naturally varies according\nto the circumstances and other sources of information of the\nperson in question, its relativeness comes to be admitted as\ninevitable, or at least it is not to be wondered at if such\nshould be the case.\n\nOn our view of Probability, therefore, its 'relativeness' in\nany given case is a misleading expression, and it will be\nfound much preferable to speak of the effect produced by\nvariations in the nature and amount of the data which we\nhave before us. Now it must be admitted that there are\nfrequently cases in our science in which such variations are\npeculiarly likely to be found. For instance, I am expecting\na friend who is a passenger in an ocean steamer. There are\na hundred passengers on board, and the crew also numbers\na hundred. I read in the papers that one person was lost by\nfalling overboard; my anticipation that it was my friend who\nwas lost is but small, of course. On turning to another\npaper, I see that the man who was lost was a passenger, not\none of the crew; my slight anxiety is at once doubled. But\nanother account adds that it was an Englishman, and on\nthat line at that season the English passengers are known\nto be few; I at once begin to entertain decided fears. And\nso on, every trifling bit of information instantly affecting my\nexpectations.\n\n15. Now since it is peculiarly characteristic of Probability,\nas distinguished from Induction, to be thus at the\nmercy, so to say, of every little fact that may be floating\nabout when we are in the act of forming our opinion, what\ncan be the harm (it may be urged) of expressing this state\nof things by terming our state of expectation _relative_?\n\nThere seem to me to be two objections. In the first place,\nas just mentioned, we are induced to reject such an expression\non grounds of consistency. It is inconsistent with the\ngeneral spirit and treatment of the subject hitherto adopted,\nand tends to divorce Probability from Inductive logic instead\nof regarding them as cognate sciences. We are aiming at\ntruth, as far as that goal can be reached by our road, and\ntherefore we dislike to regard our conclusions as relative in\nany other sense than that in which truth itself may be said\nto be relative.\n\nIn the second place, this condition of unstable assent,\nthis constant liability to have our judgment affected, to any\ndegree and at any moment, by the accession of new knowledge,\nthough doubtless characteristic of Probability, does\nnot seem to me characteristic of it in its sounder and more\nlegitimate applications. It seems rather appropriate to a\nprecipitate judgment formed in accordance with the rules,\nthan a strict example of their natural employment. Such\nprecipitate judgments may occur in the case of ordinary deductive\nconclusions. In the practical exigencies of life we\nare constantly in the habit of forming a hasty opinion with\nnearly full confidence, at any rate temporarily, upon the\nstrength of evidence which we must well know at the time\ncannot be final. We wait a short time, and something else\nturns up which induces us to alter our opinion, perhaps to\nreverse it. Here our conclusions may have been perfectly\nsound under the given circumstances, that is, they may be\nsuch as every one else would have drawn who was bound to\nmake up his mind upon the data before us, and they are\nunquestionably 'relative' judgments in the sense now under\ndiscussion. And yet, I think, every one would shrink from\nso terming them who wished systematically to carry out the\nview that Logic was to be regarded as an organon of truth.\n\n16. In the examples of Probability which we have\nhitherto employed, we have for the most part assumed that\nthere was a certain body of statistics set before us on which\nour conclusion was to rest. It was assumed, on the one\nhand, that no direct specific evidence could be got, so that\nthe judgment was really to be one of Probability, and to rest\non these statistics; in other words, that nothing better than\nthem was available for us. But it was equally assumed, on\nthe other hand, that these statistics were open to the observation\nof every one, so that we need not have to put up with\nanything inferior to them in forming our opinion. In other\nwords, we have been assuming that here, as in the case of\nmost other sciences, those who have to draw a conclusion\nstart from the same footing of opportunity and information.\nThis, for instance, clearly is or ought to be the case when\nwe are concerned with games of chance; ignorance or misapprehension\nof the common data is never contemplated\nthere. So with the statistics of life, or other insurance: so\nlong as our judgment is to be accurate (after its fashion) or\njustifiable, the common tables of mortality are all that any\none has to go by.\n\n17. It is true that in the case of a man's prospect of\ndeath we should each qualify our judgment by what we\nknew or reasonably supposed as to his health, habits, profession,\nand so on, and should thus arrive at varying estimates.\nBut no one could _justify_ his own estimate without\nappealing explicitly or implicitly to the statistical grounds on\nwhich he had relied, and if these were not previously available\nto other persons, he must now set them before their\nnotice. In other words, the judgments we entertain, here as\nelsewhere, are only relative so long as we rest them on\ngrounds peculiar to ourselves. The process of justification,\nwhich I consider to be essential to logic, has a tendency to\ncorrect such individualities of judgment, and to set all observers\non the same basis as regards their data.\n\nIt is better therefore to regard the conclusions of Probability\nas being absolute and objective, in the same sense as,\nthough doubtless in a far less degree than, they are in Induction.\nFully admitting that our conclusions will in many\ncases vary exceedingly from time to time by fresh accessions\nof knowledge, it is preferable to regard such fluctuations of\nassent as partaking of the nature of precipitate judgments,\nfounded on special statistics, instead of depending only on\nthose which are common to all observers. In calling such\njudgments precipitate it is not implied that there is any\nblame in entertaining them, but simply that, for one reason\nor another, we have been induced to form them without\nwaiting for the possession of the full amount of evidence,\nstatistical or otherwise, which might ultimately be looked\nfor. This explanation will suit the facts equally well, and is\nmore consistent with the general philosophical position maintained\nin this work.\n\n\n1. \"Is it not self-evident that internal improbabilities of all kinds\n  weaken external proof? Doubtless, but to what practical purpose can\n  this be alleged here, when it has been proved before, that real\n  internal improbabilities, which rise even to moral certainty, are\n  overcome by the most ordinary testimony.\" Part II. ch. III.\n\n2. \"Miracles must not be compared to common natural events; or to\n  events which, though uncommon, are similar to what we daily\n  experience; but to the extraordinary phenomena of nature. And then\n  the comparison will be between the presumption against miracles, and\n  the presumption against such uncommon appearances, suppose as\n  comets,\".... Part II. ch. II.\n\n3. For instance, Sir J. F. Stephen explains it by drawing a\n  distinction between chances and probabilities, which he says that\n  Butler has confused together; \"the objection that very ordinary\n  proof will overcome a presumption of millions to one is based upon a\n  confusion between probabilities and chances. The probability of an\n  event is its capability of being proved. Its chance is the numerical\n  proportion between the number of possible cases--supposed to be\n  equally favourable--favourable to its occurrence; and the number of\n  possible cases unfavourable to its occurrence\" (_General view of the\n  Criminal Law of England_, p. 255). Donkin, again (_Phil. Magazine_,\n  June, 1851), employs the terms improbability and incredibility to\n  mark the same distinction.\n\n4. In the extreme case of the witness himself merely guessing, or\n  being as untrustworthy as if he merely guessed, the two stories will\n  of course stand on precisely the same footing. This case will be\n  noticed again in Chapter XVII. It may be remarked that there are\n  several subtleties here which cannot be adequately noticed without\n  some previous investigation into the question of the credibility of\n  witnesses.\n\n5. According to Dante, something resembling this prevailed amongst the\n  occupants of the _Inferno_. The cardinals and others whom he there\n  meets are able to _give_ information about many events which were\n  yet to happen upon earth, but they had to _ask_ it for many events\n  which actually had happened.\n\n\n\n\nCHAPTER XIII.\n\n\n_ON THE CONCEPTION AND TREATMENT OF MODALITY._\n\n1. The reader who knows anything of the scholastic\nLogic will have perceived before now that we have been\ntouching in a variety of places upon that most thorny and\nrepulsive of districts in the logical territory;--modality. It\nwill be advisable, however, to put together, somewhat more\ndefinitely, what has to be said upon the subject. I propose,\ntherefore, to devote this chapter to a brief account of the\nprincipal varieties of treatment which the modals have received\nat the hands of professed logicians.\n\nIt must be remarked at the outset that the sense in\nwhich modality and modal propositions have been at various\ntimes understood, is by no means fixed and invariably the\nsame. This diversity of view has arisen partly from corresponding\ndifferences in the view taken of the province and\nnature of logic, and partly from differences in the philosophical\nand scientific opinions entertained as to the constitution\nand order of nature. In later times, moreover,\nanother very powerful agent in bringing about a change in\nthe treatment of the subject must be recognized in the\ngradual and steady growth of the theory of Probability, as\nworked out by the mathematicians from their own point of\nview.\n\n2. In spite, however, of these differences of treatment,\nthere has always been some community of subject-matter in\nthe discussions upon this topic. There has almost always\nbeen some reference to quantity of belief; enough perhaps\nto justify De Morgan's[1] remark, that Probability was \"the\nunknown God whom the schoolmen ignorantly worshipped\nwhen they so dealt with this species of enunciation, that it\nwas said to be beyond human determination whether they\nmost tortured the modals, or the modals them.\" But this\nreference to quantity of belief has sometimes been direct and\nimmediate, sometimes indirect and arising out of the nature\nof the subject-matter of the proposition. The fact is, that\nthat distinction between the purely subjective and purely objective\nviews of logic, which I have endeavoured to bring out\ninto prominence in the eleventh chapter, was not by any\nmeans clearly recognized in early times, nor indeed before\nthe time of Kant, and the view to be taken of modality\nnaturally shared in the consequent confusion. This will, I\nhope, be made clear in the course of the following chapter,\nwhich is intended to give a brief sketch of the principal\ndifferent ways in which the modality of propositions has\nbeen treated in logic. As it is not proposed to give anything\nlike a regular history of the subject, there will be no\nnecessity to adhere to any strict sequence of time, or to\ndiscuss the opinions of any writers, except those who may be\ntaken as representative of tolerably distinct views. The\noutcome of such investigation will be, I hope, to convince\nthe reader (if, indeed, he had not come to that conviction\nbefore), that the logicians, after having had a long and fair\ntrial, have failed to make anything satisfactory out of this\nsubject of the modals by their methods of enquiry and treatment;\nand that it ought, therefore, to be banished entirely\nfrom that science, and relegated to Probability.\n\n3. From the earliest study of the syllogistic process\nit was seen that, complete as that process is within its own\ndomain, the domain, at any rate under its simplest treatment,\nis a very limited one. Propositions of the pure form,--All\n(or some) A is (or is not) B,--are found in practice to form\nbut a small portion even of our categorical statements. We\nare perpetually meeting with others which express the relation\nof B to A with various degrees of necessity or probability;\ne.g. A must be B, A may be B; or the effect of\nsuch facts upon our judgment, e.g. I am perfectly certain\nthat A is B, I think that A may be B; with many others of\na more or less similar type. The question at once arises,\nHow are such propositions to be treated? It does not seem\nto have occurred to the old logicians, as to some of their successors\nin modern times, simply to reject all consideration of\nthis topic. Their faith in the truth and completeness of\ntheir system of inference was far too firm for them to suppose\nit possible that forms of proposition universally recognized\nas significant in popular speech, and forms of inference\nuniversally recognized there as valid, were to be omitted\nbecause they were inconvenient or complicated.\n\n4. One very simple plan suggests itself, and has indeed\nbeen repeatedly advocated, viz. just to transfer all that\nis characteristic of such propositions into that convenient receptacle\nfor what is troublesome elsewhere, the predicate.[2]\nHas not another so-called modality been thus got rid of?[3]\nand has it not been attempted by the same device to abolish\nthe distinctive characteristic of negative propositions, viz. by\nshifting the negative particle into the predicate? It must\nbe admitted that, up to a certain point, something may be\ndone in this way. Given the reasoning, 'Those who take\narsenic will probably die; A has taken it, therefore he will\nprobably die;' it is easy to convert this into an ordinary\nsyllogism of the pure type, by simply wording the major,\n'Those who take arsenic are people-who-will-probably-die,'\nwhen the conclusion follows in the same form, 'A is one\nwho-will-probably-die.' But this device will only carry us\na very little way. Suppose that the minor premise also is\nof the same modal description, e.g. 'A has probably taken\narsenic,' and it will be seen that we cannot relegate the\nmodality here also to the predicate without being brought to\na stop by finding that there are four terms in the syllogism.\n\nBut even if there were not this particular objection, it\ndoes not appear that anything is to be gained in the way of\nintelligibility or method by such a device as the above. For\nwhat is meant by a modal predicate, by the predicate\n'probably mortal,' for instance, in the proposition 'All poisonings\nby arsenic are probably mortal'? If the analogy with\nordinary pure propositions is to hold good, it must be a\npredicate referring to the _whole_ of the subject, for the subject\nis distributed. But then we are at once launched into\nthe difficulties discussed in a former chapter (Ch. VI. \u00a7\u00a719-25),\nwhen we attempt to justify or verify the application of\nthe predicate. We have to enquire (at least on the view\nadopted in this work) whether the application of the predicate\n'probably mortal' to the _whole_ of the subject, really\nmeans at bottom anything else than that the predicate\n'mortal' is to be applied to a _portion_ (more than half) of the\nmembers denoted by the subject. When the transference of\nthe modality to the predicate raises such intricate questions\nas to the sense in which the predicate is to be interpreted,\nthere is surely nothing gained by the step.\n\n5. A second, and more summary way of shelving all\ndifficulties of the subject, so far at least as logic, or the\nwriters upon logic, are concerned, is found by simply denying\nthat modality has any connection whatever with logic. This\nis the course adopted by many modern writers, for instance,\nby Hamilton and Mansel, in reference to whom one cannot\nhelp remarking that an unduly large portion of their logical\nwritings seems occupied with telling us what does _not_ belong\nto logic. They justify their rejection on the ground that\nthe mode belongs to the matter, and must be determined by\na consideration of the matter, and therefore is extralogical.\nTo a certain extent I agree with their grounds of rejection,\nfor (as explained in Chapter VI.) it is not easy to see how\nthe degree of modality of any proposition, whether premise\nor conclusion, can be justified without appeal to the matter.\nBut then questions of justification, in any adequate sense of\nthe term, belong to a range of considerations somewhat alien\nto Hamilton's and Mansel's way of regarding the science.\nThe complete justification of our inferences is a matter\nwhich involves their truth or falsehood, a point with which\nthese writers do not much concern themselves, being only\noccupied with the consistency of our reasonings, not with\ntheir conformity with fact. Were I speaking as a Hamiltonian\nI should say that modality _is_ formal rather than\nmaterial, for though we cannot justify the degree of our\nbelief of a proposition without appeal to the matter, we can\nto a moderate degree of accuracy estimate it without any\nsuch appeal; and this would seem to be quite enough to\nwarrant its being regarded as formal.\n\nIt must be admitted that Hamilton's account of the\nmatter when he is recommending the rejection of the modals,\nis not by any means clear and consistent. He not only fails,\nas already remarked, to distinguish between the formal and\nthe material (in other words, the true and the false) modality;\nbut when treating of the former he fails to distinguish\nbetween the extremely diverse aspects of modality when\nviewed from the Aristotelian and the Kantian stand-points.\nOf the amount and significance of this difference we shall\nspeak presently, but it may be just pointed out here that\nHamilton begins (Vol. I. p. 257) by rejecting the modals on\nthe ground that the distinctions between the necessary, the\ncontingent, the possible, and the impossible, must be wholly\nrested on an appeal to the matter of the propositions, in\nwhich he is, I think, quite correct. But then a little further\non (p. 260), in explaining 'the meaning of three terms which\nare used in relation to pure and modal propositions,' he gives\nthe widely different Kantian, or three-fold division into the\napodeictic, the assertory, and the problematic. He does not\ntake the precaution of pointing out to his hearers the very\ndifferent general views of logic from which these two accounts\nof modality spring.[4]\n\n6. There is one kind of modal syllogism which it\nwould seem unreasonable to reject on the ground of its not\nbeing formal, and which we may notice in passing. The\npremise 'Any A is probably B,' is equivalent to 'Most A are B.'\nNow it is obvious that from two such premises as 'Most A\nare B,' 'Most A are C,' we can deduce the consequence,\n'Some C are B.' Since this holds good whatever may be\nthe nature of A, B, and C, it is, according to ordinary usage\nof the term, a formal syllogism. Mansel, however, refuses to\nadmit that any such syllogisms belong to formal logic. His\nreasons are given in a rather elaborate review[5] and criticism\nof some of the logical works of De Morgan, to whom the\nintroduction of 'numerically definite syllogisms' is mainly\ndue. Mansel does not take the particular example given\nabove, as he is discussing a somewhat more comprehensive\nalgebraic form. He examines it in a special numerical\nexample:[6]--18 out of 21 Ys are X; 15 out of 21 Ys are Z;\nthe conclusion that 12 Zs are X is rejected from formal logic\non the ground that the arithmetical judgment involved is\nsynthetical, not analytical, and rests upon an intuition of\nquantity. We cannot enter upon any examination of these\nreasons here; but it may merely be remarked that his\ncriticism demands the acceptance of the Kantian doctrines\nas to the nature of arithmetical judgments, and that it would\nbe better to base the rejection not on the ground that the\nsyllogism is not _formal_, but on the ground that it is not\n_analytical_.\n\n7. There is another and practical way of getting rid\nof the perplexities of modal reasoning which must be noticed\nhere. It is the resource of ordinary reasoners rather than the\ndecision of professed logicians,[7] and, like the first method of\nevasion already pointed out in this chapter, is of very partial\napplication. It consists in treating the premises, during the\nprocess of reasoning, as if they were pure, and then reintroducing\nthe modality into the conclusion, as a sort of\nqualification of its full certainty. When each of the premises\nis nearly certain, or when from any cause we are not\nconcerned with the extent of their departure from full certainty,\nthis rough expedient will answer well enough. It is,\nI apprehend, the process which passes through the minds of\nmost persons in such cases, in so far as they reason consciously.\nThey would, presumably, in such an example as that previously\ngiven (\u00a74), proceed as if the premises that 'those\nwho take arsenic will die,' and that 'the man in question\nhas taken it,' were quite true, instead of being only probably\ntrue, and they would consequently draw the conclusion that\n'he would die.' But bearing in mind that the premises are\nnot certain, they would remember that the conclusion was\nonly to be held with a qualified assent. This they would\nexpress quite correctly, if the mere nature and not the\ndegree of that assent is taken into account, by saying that\n'he is likely to die.' In this case the modality is rejected\ntemporarily from the premises to be reintroduced into the\nconclusion.\n\nIt is obvious that such a process as this is of a very\nrough and imperfect kind. It does, in fact, omit from accurate\nconsideration just the one point now under discussion.\nIt takes no account of the varying shades of expression by\nwhich the degree of departure from perfect conviction is\nindicated, which is of course the very thing with which\nmodality is intended to occupy itself. At best, therefore, it\ncould only claim to be an extremely rude way of deciding\nquestions, the accurate and scientific methods of treating\nwhich are demanded of us.\n\n8. In any employment of applied logic we have of\ncourse to go through such a process as that just mentioned.\nOutside of pure mathematics it can hardly ever be the case\nthat the premises from which we reason are held with absolute\nconviction. Hence there must be a lapse from absolute\nconviction in the conclusion. But we reason on the hypothesis\nthat the premises are true, and any trifling defection\nfrom certainty, of which we may be conscious, is mentally\nreserved as a qualification to the conclusion. But such considerations\nas these belong rather to ordinary applied logic;\nthey amount to nothing more than a caution or hint to be\nborne in mind when the rules of the syllogism, or of induction,\nare applied in practice. When, however, we are\ntreating of modality, the extent of the defection from full\ncertainty is supposed to be sufficiently great for our language\nto indicate and appreciate it. What we then want is of\ncourse a scientific discussion of the principles in accordance\nwith which this departure is to be measured and expressed,\nboth in our premises and in our conclusion. Such a plan\ntherefore for treating modality, as the one under discussion,\nis just as much a banishment of it from the field of real\nlogical enquiry, as if we had determined avowedly to reject it\nfrom consideration.\n\n9. Before proceeding to a discussion of the various\nways in which modality may be treated by those who admit\nit into logic, something must be said to clear up a possible\nsource of confusion in this part of the subject. In the\ncases with which we have hitherto been mostly concerned,\nin the earlier chapters of this work, the characteristic of\nmodality (for in this chapter we may with propriety use this\nlogical term) has generally been found in singular and particular\npropositions. It presented itself when we had to\njudge of individual cases from a knowledge of the average,\nand was an expression of the fact that the proposition relating\nto these individuals referred to a portion only of the\nwhole class from which the average was taken. Given that\nof men of fifty-five, three out of five will die in the course of\ntwenty years, we have had to do with propositions of the\nvague form, 'It is probable that AB (of that age) will die,'\nor of the more precise form, 'It is three to two that AB will\ndie,' within the specified time. Here the modal proposition\nnaturally presents itself in the form of a singular or particular\nproposition.\n\n10. But when we turn to ordinary logic we may find\n_universal_ propositions spoken of as modal. This must mostly\nbe the case with those which are termed necessary or impossible,\nbut it may also be the case with the probable. We\nmay meet with the form 'All X is probably Y.' Adopting\nthe same explanation here as has been throughout adopted in\nanalogous cases, we must say that what is meant by the\nmodality of such a proposition is the proportional number of\ntimes in which the universal proposition would be correctly\nmade. And in this there is, so far, no difficulty. The only\ndifference is that whereas the justification of the former, viz.\nthe particular or individual kind of modal, was obtainable\nwithin the limits of the universal proposition which included\nit, the justification of the modality of a universal proposition\nhas to be sought in a group or succession of other propositions.\nThe proposition has to be referred to some group of\nsimilar ones and we have to consider the proportion of cases\nin which it will be true. But this distinction is not at all\nfundamental.\n\nIt is quite true that universal propositions from their\nnature are much less likely than individual ones to be justified,\nin practice, by such appeal. But, as has been already\nfrequently pointed out, we are not concerned with the way\nin which our propositions are practically obtained, nor with\nthe way in which men might find it most natural to test\nthem; but with that ultimate justification to which we appeal\nin the last resort, and which has been abundantly shown\nto be of a statistical character. When, therefore, we say that\n'it is probable that all X is Y,' what we mean is, that in\nmore than half the cases we come across we should be right\nin so judging, and in less than half the cases we should be\nwrong.\n\n11. It is at this step that the possible ambiguity is\nencountered. When we talk of the chance that All X is Y,\nwe contemplate or imply the complementary chance that it is\nnot so. Now this latter alternative is not free from ambiguity.\nIt might happen, for instance, in the cases of failure,\nthat no X is Y, or it might happen that some X, only, is not Y;\nfor both of these suppositions contradict the original proposition,\nand are therefore instances of its failure. In practice,\nno doubt, we should have various recognized rules and\ninductions to fall back upon in order to decide between these\nalternatives, though, of course, the appeal to them would be\nin strictness extralogical. But the mere existence of such an\nambiguity, and the fact that it can only be cleared up by\nappeal to the subject-matter, are in themselves no real\ndifficulty in the application of the conception of modality to\nuniversal propositions as well as to individual ones.\n\n12. Having noticed some of the ways in which the\nintroduction of modality into logic has been evaded or rejected,\nwe must now enter into a brief account of its treatment\nby those who have more or less deliberately admitted\nits claims to acceptance.\n\nThe first enquiry will be, What opinions have been held\nas to the nature of modality? that is, Is it primarily an affection\nof the matter of the proposition, and, if not, what is it\nexactly? In reference to this enquiry it appears to me, as\nalready remarked, that amongst the earlier logicians no such\nclear and consistent distinction between the subjective and\nobjective views of logic as is now commonly maintained, can\nbe detected.[8] The result of this appears in their treatment\nof modality. This always had some reference to the subjective\nside of the proposition, viz. in this case to the nature\nor quantity of the belief with which it was entertained; but\nit is equally clear that this characteristic was not estimated\nat first hand, so to say, and in itself, but rather from a consideration\nof the matter determining what it should be. The\ncommonly accepted scholastic or Aristotelian division, for\ninstance, is into the necessary, the contingent, the possible,\nand the impossible. This is clearly a division according to\nthe matter almost entirely, for on the purely mental side the\nnecessary and the impossible would be just the same; one\nimplying full conviction of the truth of a proposition, and the\nother of that of its contradictory. So too, on the same side, it\nwould not be easy to distinguish between the contingent and\nthe possible. On the view in question, therefore, the modality\nof a proposition was determined by a reference to the nature\nof the subject-matter. In some propositions the nature of\nthe subject-matter decided that the predicate was necessarily\njoined to the subject; in others that it was impossible that\nthey should be joined; and so on.\n\n13. The artificial character of such a four-fold division\nwill be too obvious to modern minds for it to be necessary to\ncriticize it. A very slight study of nature and consequent\nappreciation of inductive evidence suffice to convince us that\nthose uniformities upon which all connections of phenomena,\nwhether called necessary or contingent, depend, demand extremely\nprofound and extensive enquiry; that they admit of\nno such simple division into clearly marked groups; and\nthat, therefore, the pure logician had better not meddle with\nthem.[9]\n\nThe following extract from Grote's _Aristotle_ (Vol. I. p. 192)\nwill serve to show the origin of this four-fold division,\nits conformity with the science of the day, and consequently\nits utter want of conformity with that of our own time:--\"The\ndistinction of Problematical and Necessary Propositions\ncorresponds, in the mind of Aristotle, to that capital and\ncharacteristic doctrine of his Ontology and Physics, already\ntouched on in this chapter. He thought, as we have seen,\nthat in the vast circumferential region of the Kosmos, from\nthe outer sidereal sphere down to the lunar sphere, celestial\nsubstance was a necessary existence and energy, sempiternal\nand uniform in its rotations and influence; and that through\nits beneficent influence, pervading the concavity between the\nlunar sphere and the terrestrial centre (which included the\nfour elements with their compounds) there prevailed a regularizing\ntendency called Nature; modified, however, and\npartly counteracted by independent and irregular forces called\nSpontaneity and Chance, essentially unknowable and unpredictable.\nThe irregular sequences thus named by Aristotle\nwere the objective correlate of the Problematical Proposition\nin Logic. In these sublunary sequences, as to future time,\n_may or may not_, was all that could be attained, even by the\nhighest knowledge; certainty, either of affirmation or negation,\nwas out of the question. On the other hand, the necessary\nand uniform energies of the celestial substance, formed\nthe objective correlate of the Necessary Proposition in Logic;\nthis substance was not merely an existence, but an existence\nnecessary and unchangeable... he considers the Problematical\nProposition in Logic to be not purely subjective, as an\nexpression of the speaker's ignorance, but something more,\nnamely, to correlate with an objective essentially unknowable\nto all.\"\n\n14. Even after this philosophy began to pass away,\nthe divisions of modality originally founded upon it might\nhave proved, as De Morgan has remarked,[10] of considerable\nservice in medi\u00e6val times. As he says, people were much\nmore frequently required to decide in one way or the other\nupon a single testimony, without there being a sufficiency of\nspecific knowledge to test the statements made. The old\nlogician \"did not know but that any day of the week might\nbring from Cathay or Tartary an account of men who ran on\nfour wheels of flesh and blood, or grew planted in the ground,\nlike Polydorus in the \u00c6neid, as well evidenced as a great\nmany nearly as marvellous stories.\" Hence, in default of\nbetter inductions, it might have been convenient to make\nrough classifications of the facts which were and which were\nnot to be accepted on testimony (the necessary, the impossible, &c.),\nand to employ these provisional inductions (which\nis all we should now regard them) as testing the stories\nwhich reached him. Propositions belonging to the class of\nthe impossible might be regarded as having an antecedent\npresumption against them so great as to prevail over almost\nany testimony worth taking account of, and so on.\n\n15. But this old four-fold division of modals continued\nto be accepted and perpetuated by the logicians long\nafter all philosophical justification for it had passed away.\nSo far as I have been able to ascertain, scarcely any logician\nof repute or popularity before Kant, was bold enough to\nmake any important change in the way of regarding them.[11]\nEven the Port-Royal Logic, founded as it is on Cartesianism,\nrepeats the traditional statements, though with extreme\nbrevity. This adherence to the old forms led, it need not be\nremarked, to considerable inconsistency and confusion in\nmany cases. These forms were founded, as we have seen, on\nan objective view of the province of logic, and this view was\nby no means rigidly carried out in many cases. In fact it\nwas beginning to be abandoned, to an extent and in directions\nwhich we have not opportunity here to discuss, before\nthe influence of Kant was felt. Many, for instance, added to\nthe list of the four, by including the true and the false;\noccasionally also the probable, the supposed, and the certain\nwere added. This seems to show some tendency towards\nabandoning the objective for the subjective view, or at least\nindicates a hesitation between them.\n\n16. With Kant's view of modality almost every one is\nfamiliar. He divides judgments, under this head, into the\napodeictic, the assertory, and the problematic. We shall have\nto say something about the number and mutual relations of\nthese divisions presently; we are now only concerned with\nthe general view which they carry out. In this respect it will\nbe obvious at once what a complete change of position has\nbeen reached. The 'necessary' and the 'impossible' demanded\nan appeal to the matter of a proposition in order to\nrecognize them; the 'apodeictic' and the 'assertory', on the\nother hand, may be true of almost any matter, for they\ndemand nothing but an appeal to our consciousness in order\nto distinguish between them. Moreover, the distinction\nbetween the assertory and the problematic is so entirely\nsubjective and personal, that it may vary not only between\none person and another, but in the case of the same person\nat different times. What one man knows to be true, another\nmay happen to be in doubt about. The apodeictic judgment\nis one which we not only accept, but which we find ourselves\nunable to reverse in thought; the assertory is simply accepted;\nthe problematic is one about which we feel in\ndoubt.\n\nThis way of looking at the matter is the necessary outcome\nof the conceptualist or Kantian view of logic. It has\nbeen followed by many logicians, not only by those who may\nbe called followers of Kant, but by almost all who have felt\nhis influence. Ueberweg, for instance, who is altogether at\nissue with Kant on some fundamental points, adopts it.\n\n17. The next question to be discussed is, How many\nsubdivisions of modality are to be recognized? The Aristotelian\nor scholastic logicians, as we have seen, adopted a four-fold\ndivision. The exact relations of some of these to each\nother, especially the possible and the contingent, is an extremely\nobscure point, and one about which the commentators\nare by no means agreed. As, however, it seems tolerably\nclear that it was not consciously intended by the use of these\nfour terms to exhibit a graduated scale of intensity of conviction,\ntheir correspondence with the province of modern\nprobability is but slight, and the discussion of them, therefore,\nbecomes rather a matter of special or antiquarian interest.\nDe Morgan, indeed (_Formal Logic_, p. 232), says that\nthe schoolmen understood by contingent more likely than\nnot, and by possible less likely than not. I do not know\non what authority this statement rests, but it credits them\nwith a much nearer approach to the modern views of probability\nthan one would have expected, and decidedly nearer than\nthat of most of their successors.[12] The general conclusion at\nwhich I have arrived, after a reasonable amount of investigation,\nis that there were two prevalent views on the subject.\nSome (e.g. Burgersdyck, Bk. I. ch. 32) admitted that there\nwere at bottom only two kinds of modality; the contingent\nand the possible being equipollent, as also the necessary and\nthe impossible, provided the one asserts and the other\ndenies. This is the view to which those would naturally\nbe led who looked mainly to the nature of the subject-matter.\nOn the other hand, those who looked mainly at the form of\nexpression, would be led by the analogy of the four forms of\nproposition, and the necessity that each of them should stand\nin definite opposition to each other, to insist upon a distinction\nbetween the four modals.[13] They, therefore, endeavoured\nto introduce a distinction by maintaining (e.g. Crackanthorpe,\nBk. III. ch. 11) that the contingent is that which now is but\nmay not be, and the possible that which now is not but may\nbe. A few appear to have made the distinction correspondent\nto that between the physically and the logically\npossible.\n\n18. When we get to the Kantian division we have\nreached much clearer ground. The meaning of each of these\nterms is quite explicit, and it is also beyond doubt that they\nhave a more definite tendency in the direction of assigning a\ngraduated scale of conviction. So long as they are regarded\nfrom a metaphysical rather than a logical standing point,\nthere is much to be said in their favour. If we use introspection\nmerely, confining ourselves to a study of the judgments\nthemselves, to the exclusion of the grounds on which\nthey rest, there certainly does seem a clear and well-marked\ndistinction between judgments which we cannot even conceive\nto be reversed in thought; those which we could\nreverse, but which we accept as true; and those which we\nmerely entertain as possible.\n\nRegarded, however, as a logical division, Kant's arrangement\nseems to me of very little service. For such logical\npurposes indeed, as we are now concerned with, it really\nseems to resolve itself into a _two_-fold division. The distinction\nbetween the apodeictic and the assertory will be\nadmitted, I presume, even by those who accept the metaphysical\nor psychological theory upon which it rests, to be a\ndifference which concerns, not the quantity of belief with\nwhich the judgments are entertained, but rather the violence\nwhich would have to be done to the mind by the attempt to\nupset them. Each is fully believed, but the one can, and\nthe other cannot, be controverted. The belief with which an\nassertory judgment is entertained is full belief, else it would\nnot differ from the problematic; and therefore in regard to\nthe quantity of belief, as distinguished from the quality or\ncharacter of it, there is no difference between it and the apodeictic.\nIt is as though, to offer an illustration, the index\nhad been already moved to the top of the scale in the assertory\njudgment, and all that was done to convert this into\nan apodeictic one, was to _clamp_ it there. The only logical\ndifference which then remains is that between problematic\nand assertory, the former comprehending all the judgments\nas to the truth of which we have any degree of doubt, and\nthe latter those of which we have no doubt. The whole\nrange of the former, therefore, with which Probability is\nappropriately occupied, is thrown undivided into a single\ncompartment. We can hardly speak of a 'division' where\none class includes everything up to the boundary line, and\nthe other is confined to that boundary line. Practically,\ntherefore, on this view, modality, as the mathematical student\nof Probability would expect to find it, as completely\ndisappears as if it were intended to reject it.\n\n19. By less consistent and systematic thinkers, and\nby those in whom ingenuity was an over prominent feature,\na variety of other arrangements have been accepted or proposed.\nThere is, of course, some justification for such attempts\nin the laudable desire to bring our logical forms into better\nharmony with ordinary thought and language. In practice,\nas was pointed out in an earlier chapter, every one recognizes\na great variety of modal forms, such as 'likely,' 'very\nlikely,' 'almost certainly,' and so on almost without limit in\neach direction. It was doubtless supposed that, by neglecting\nto make use of technical equivalents for some of these\nforms, we should lose our logical control over certain possible\nkinds of inference, and so far fall short even of the precision\nof ordinary thought.\n\nWith regard to such additional forms, it appears to me\nthat all those which have been introduced by writers who\nwere uninfluenced by the Theory of Probability, have done\nlittle else than create additional confusion, as such writers do\nnot attempt to marshal their terms in order, or to ascertain\ntheir mutual relations. Omitting, of course, forms obviously\nof material modality, we have already mentioned the true\nand the false; the probable, the supposed, and the certain.\nThese subdivisions seem to have reached their climax at a\nvery early stage in Occam (Prantl, III. 380), who held that a\nproposition might be modally affected by being 'vera, scita,\nfalsa, ignota, scripta, prolata, concepta, credita, opinata, dubitata.'\n\n20. Since the growth of the science of Probability,\nlogicians have had better opportunities of knowing what\nthey had to aim at; and, though it cannot be said that their\nattempts have been really successful, these are at any rate a\ndecided improvement upon those of their predecessors. Dr\nThomson,[14] for instance, gives a nine-fold division. He says\nthat, arranging the degrees of modality in an ascending\nscale, we find that a judgment may be either possible,\ndoubtful, probable, morally certain for the thinker himself,\nmorally certain for a class or school, morally certain for all,\nphysically certain with a limit, physically certain without\nlimitation, and mathematically certain. Many other divisions\nmight doubtless be mentioned, but, as every mathematician\nwill recognize, the attempt to secure any general\nagreement in such a matter of arrangement is quite hopeless.\nIt is here that the beneficial influence of the mathematical\ntheory of Probability is to be gratefully acknowledged. As\nsoon as this came to be studied it must have been perceived\nthat in attempting to mark off clearly from one another\ncertain gradations of belief, we should be seeking for breaches\nin a continuous magnitude. In the advance from a slight\npresumption to a strong presumption, and from that to moral\ncertainty, we are making a gradual ascent, in the course of\nwhich there are no natural halting-places. The proof of this\ncontinuity need not be entered upon here, for the materials\nfor it will have been gathered from almost every chapter of\nthis work. The reader need merely be reminded that the\ngrounds of our belief, in all cases which admit of number and\nmeasurement, are clearly seen to be of this description; and\nthat therefore unless the belief itself is to be divorced from\nthe grounds on which it rests, what thus holds as to their\ncharacteristics must hold also as to its own.\n\nIt follows, therefore, that modality in the old sense of the\nword, wherein an attempt was made to obtain certain natural\ndivisions in the scale of conviction, must be finally abandoned.\nAll that it endeavoured to do can now be done incomparably\nbetter by the theory of Probability, with its numerical scale\nwhich admits of indefinite subdivision. None of the old systems\nof division can be regarded as a really natural one;\nthose which admit but few divisions being found to leave the\nwhole range of the probable in one unbroken class, and those\nwhich adopt many divisions lapsing into unavoidable vagueness\nand uncertainty.\n\n21. Corresponding to the distinction between pure\nand modal propositions, but even more complicated and\nunsatisfactory in its treatment, was that between pure and\nmodal syllogisms. The thing discussed in the case of the\nlatter was, of course, the effect produced upon the conclusion\nin respect of modality, by the modal affection of one or both\npremises. It is only when we reach such considerations as\nthese that we are at all getting on to the ground appropriate\nto Probability; but it is obvious that very little could be\ndone with such rude materials, and the inherent clumsiness\nand complication of the whole modal system come out very\nclearly here. It was in reference probably to this complication\nthat some of the bitter sayings[15] of the schoolmen and\nothers which have been recorded, were uttered.\n\nAristotle has given an intricate investigation of this subject,\nand his followers naturally were led along a similar\ntrack. It would be quite foreign to my purpose in the slight\nsketch in this chapter to attempt to give any account of\nthese enquiries, even were I competent to do so; for, as has\nbeen pointed out, the connection between the Aristotelian\nmodals and the modern view of the nature of Probability,\nthough real, is exceedingly slight. It need only be remarked\nthat what was complicated enough with four modals to be\ntaken account of, grows intricate beyond all endurance when\nsuch as the 'probable' and the 'true' and the 'false' have\nalso to be assigned a place in the list. The following examples[16]\nwill show the kind of discussions with which the logicians\nexercised themselves. 'Whether, with one premise\ncertain, and the other probable, a certain conclusion may be\ninferred': 'Whether, from the impossible, the necessary can\nbe inferred'; 'Whether, with one premise necessary and the\nother _de inesse_, the conclusion is necessary', and so on,\nendlessly.\n\n22. On the Kantian view of modality the discussion\nof such kinds of syllogisms becomes at once decidedly more\nsimple (for here but three modes are recognized), and also\nsomewhat more closely connected with strict Probability, (for\nthe modes are more nearly of the nature of gradations of\nconviction). But, on the other hand, there is less justification\nfor their introduction, as logicians might really be expected\nto know that what they are aiming to effect by their clumsy\ncontrivances is the very thing which Probability can carry\nout to the highest desired degree of accuracy. The former\nmethods are as coarse and inaccurate, compared with the\nlatter, as were the roughest measurements of Babylonian\nnight-watchers compared with the refined calculations of the\nmodern astronomer. It is indeed only some of the general\nadherents of the Kantian Logic who enter upon any such\nconsiderations as these; some, such as Hamilton and Mansel,\nentirely reject them, as we have seen. By those who do\ntreat of the subject, such conclusions as the following are laid\ndown; that when both premises are apodeictic the conclusion\nwill be the same; so when both are assertory or problematic.\nIf one is apodeictic and the other assertory, the latter, or\n'weaker,' is all that is to be admitted for the conclusion;\nand so on. The English reader will find some account of\nthese rules in Ueberweg's _Logic_.[17]\n\n23. But although those modals, regarded as instruments\nof accurate thought, have been thus superseded by the\nprecise arithmetical expressions of Probability, the question\nstill remains whether what may be termed our popular modal\nexpressions could not be improved and adapted to more\naccurate use. It is true that the attempt to separate them\nfrom one another by any fundamental distinctions is futile,\nfor the magnitude of which they take cognizance is, as we\nhave remarked, continuous; but considering the enormous\nimportance of accurate terminology, and of recognizing\nnumerical distinctions wherever possible, it would be a real\nadvance if any agreement could be arrived at with regard to\nthe use of modal expressions. We have already noticed (Ch. II. \u00a716)\nsome suggestions by Mr Galton as to the possibility\nof a natural system of classification, resting upon the regularity\nwith which most kinds of magnitudes tend to group\nthemselves about a mean. It might be proposed, for instance,\nthat we should agree to apply the term 'good'\nto the first quarter, measuring from the best downwards;\n'indifferent' to the middle half, and 'bad' to the last quarter.\nThere seems no reason why a similarly improved terminology\nshould not some day be introduced into the ordinary modal\nlanguage of common life. It might be agreed, for instance,\nthat 'very improbable' should as far as possible be confined\nto those events which had odds of (say) more than 99 to 1\nagainst them; and so on, with other similar expressions.\nThere would, no doubt, be difficulties in the way, for in all\napplications of classification we have to surmount the two-fold\nobstacles which lie in the way, firstly (to use Kant's\nexpression) of the faculty of making rules, and secondly of\nthat of subsumption under rules. That is to say, even if we\nhad agreed upon our classes, there would still be much doubt\nand dispute, in the case of things which did not readily lend\nthemselves to be counted or measured, as to whether the\nodds were more or less than the assigned quantity.\n\nIt is true that when we know the odds for or against an\nevent, we can always state them explicitly without the necessity\nof first agreeing as to the usage of terms which shall\nimply them. But there would often be circumlocution and\npedantry in so doing, and as long as modal terms are in\npractical use it would seem that there could be no harm, and\nmight be great good, in arriving at some agreement as to the\ndegree of probability which they should be generally understood\nto indicate. Bentham, as is well known, in despair of\never obtaining anything accurate out of the language of common\nlife on this subject, was in favour of a direct appeal to\nthe numerical standard. He proposed the employment, in\njudicial trials, of an instrument, graduated from 0 to 10, on\nwhich scale the witness was to be asked to indicate the degree\nof his belief of the facts to which he testified: similarly\nthe judge might express the force with which he held his\nconclusion. The use of such a numerical scale, however, was\nto be optional only, not compulsory, as Bentham admitted\nthat many persons might feel at a loss thus to measure the\ndegree of their belief. (_Rationale of Judicial Evidence_,\nBk. I., Ch. VI.)\n\n24. Throughout this chapter we have regarded the\nmodals as the nearest counterpart to modern Probability\nwhich was afforded by the old systems of logic. The reason\nfor so regarding them is, that they represented some slight\nattempt, rude as it was, to recognize and measure certain\ngradations in the degree of our conviction, and to examine\nthe bearing of such considerations upon our logical inferences.\n\nBut although it is amongst the modals that the germs of\nthe methods of Probability are thus to be sought; the true\nsubject-matter of our science, that is, the classes of objects\nwith which it is most appropriately concerned, are rather\nrepresented by another part of the scholastic logic. This\nwas the branch commonly called Dialectic, in the old sense\nof that term. Dialectic, according to Aristotle, seems to\nhave been a sort of sister art to Rhetoric. It was concerned\nwith syllogisms differing in no way from demonstrative syllogisms,\nexcept that their premises were probable instead of\ncertain. Premises of this kind he termed topics, and the\nsyllogisms which dealt with them enthymemes. They were\nsaid to start from 'signs and likelihoods' rather than from\naxioms.[18]\n\n25. The terms in which such reasonings are commonly\ndescribed sound very much like those applicable to\nProbability, as we now understand it. When we hear of\nlikelihood, and of probable syllogisms, our first impression\nmight be that the inferences involved would be of a similar\ncharacter.[19] This, however, would be erroneous. In the\nfirst place the province of this Dialectic was much too wide,\nfor it covered in addition the whole field of what we should\nnow term Scientific or Material Induction. The distinctive\ncharacteristic of the dialectic premises was their want of\ncertainty, and of such uncertain premises Probability (as I\nhave frequently insisted) takes account of one class only,\nInduction concerning itself with another class. Again, not the\nslightest attempt was made to enter upon the enquiry, _How_\nuncertain are the premises? It is only when this is attempted\nthat we can be considered to enter upon the field of\nProbability, and it is because, after a rude fashion, the modals\nattempted to grapple with this problem, that we have regarded\nthem as in any way occupied with our special subject-matter.\n\n26. Amongst the older logics with which I have made\nany acquaintance, that of Crackanthorpe gives the fullest discussion\nupon this subject. He divides his treatment of the\nsyllogism into two parts, occupied respectively with the 'demonstrative'\nand the 'probable' syllogism. To the latter a\nwhole book is devoted. In this the nature and consequences\nof thirteen different 'loci'[20] are investigated, though it is not\nvery clear in what sense they can every one of them be regarded\nas being 'probable.'\n\nIt is doubtless true, that if the old logicians had been\nin possession of such premises as modern Probability is concerned\nwith, and had adhered to their own way of treating\nthem, they would have had to place them amongst such _loci_,\nand thus to make the consideration of them a part of their\nDialectic. But inasmuch as there does not seem to have\nbeen the slightest attempt on their part to do more here\nthan recognize the _fact_ of the premises being probable; that\nis, since it was not attempted to _measure_ their probability\nand that of the conclusion, I cannot but regard this part of\nLogic as having only the very slightest relation to Probability\nas now conceived. It seems to me little more than\none of the ways (described at the commencement of this\nchapter) by which the problem of Modality is not indeed rejected,\nbut practically evaded.\n\n27. As Logic is not the only science which is directly\nand prominently occupied with questions about belief and\nevidence, so the difficulties which have arisen there have\nbeen by no means unknown elsewhere. In respect of the\nmodals, this seems to have been manifestly the case in Jurisprudence.\nSome remarks, therefore, may be conveniently\nmade here upon this application of the subject, though of\ncourse with the brevity suitable on the part of a layman who\nhas to touch upon professional topics.\n\nRecall for a moment what are the essentials of modality.\nThese I understand to be the attempt to mark off from one\nanother, without any resort to numerical notation, varying\ndegrees of conviction or belief, and to determine the consequent\neffect of premises, thus affected, upon our conclusions.\nMoreover, as we cannot construct or retain a scale of any\nkind without employing a standard from and by which to\nmeasure it, the attainment and recognition of a standard of\ncertainty, or of one of the other degrees of conviction, is\nalmost inseparably involved in the same enquiry. In this\nsense of the term, modal difficulties have certainly shown\nthemselves in the department of Law. There have been\nsimilar attempts here, encountered by similar difficulties, to\ncome to some definite agreement as to a scale of arrangement\nof the degrees of our assent. It is of course much\nmore practicable to secure such agreement in the case of a\nspecial science, confined more or less to the experts, than in\nsubjects into which all classes of outsiders have almost equal\nright of entry. The range of application under the former\ncircumstances is narrower, and the professional experts have\nacquired habits and traditions by which the standards may\nbe retained in considerable integrity. It does not appear,\nhowever, according to all accounts, as if any very striking\nsuccess had been attained in this direction by the lawyers.\n\n28. The difficulty in its scientific, or strictly jurisprudential\nshape, seems to have shown itself principally in the\nattempt to arrange legal evidence into classes in respect of\nthe degree of its cogency. This, I understand, was the case\nin the Roman law, and in some of the continental systems of\njurisprudence which took their rise from the Roman law.\n\"The direct evidence of so many witnesses was _plena probatio_.\nThen came _minus plena probatio_, then _semiplen\u00e2\nmajor_ and _semiplen\u00e2 minor_; and by adding together a\ncertain number of half-proofs--for instance, by the production\nof a tradesman's account-books, _plus_ his supplementary\noath--full proof might be made out. It was on\nthis principle that torture was employed to obtain a confession.\nThe confession was evidence suppletory to the circumstances\nwhich were held to justify its employment.\"[21]\n\nAccording to Bentham,[22] the corresponding scale in the\nEnglish school was:--Positive proof, Violent presumption.\nProbable presumption, Light or Rash presumption. Though\nadmitted by Blackstone and others, I understand that these\ndivisions are not at all generally accepted at the present\nday.\n\n29. In the above we are reminded rather of modal\nsyllogisms. The principal practical form in which the difficulty\nunderlying the simple modal propositions presents\nitself, is in the attempt to obtain some criterion of judicial\ncertainty. By 'certainty' here we mean, of course, not what\nthe metaphysicians term apodeictic,[23] for that can seldom or\nnever be secured in practical affairs, but such a degree of\nconviction, short of this, as every reasonable person will feel\nto be sufficient for all his wants. Here again, one would\nthink, the quest must appear, to accurate thinkers, an utterly\nhopeless one; an effort to discover natural breaks in a continuous\nmagnitude. There cannot indeed be the least doubt\nthat, amongst limited classes of keen and practised intellects,\na standard of certainty, as of everything else, might be retained\nand handed down with considerable accuracy: this is\npossible in matters of taste and opinion where personal peculiarities\nof judgment are far more liable to cause disagreement\nand confusion. But then such a consensus is almost entirely\nan affair of tact and custom; whereas what is wanted in the\ncase in question is some criterion to which the comparatively\nuninitiated may be able to appeal. The standard, therefore,\nmust not merely be retained by recollection, but be generally\nrecognizable by its characteristics. If such a criterion could\nbe secured, its importance could hardly be overrated. But\nso far as one may judge from the speeches of counsel, the\ncharges of judges, and the verdicts of juries, nothing really\ndeserving the name is ever attained.\n\n30. The nearest approach, perhaps, to a recognized\nstandard is to be found in the frequent assurance that juries\nare not bound to convict only in case they have _no_ doubt of\nthe guilt of the accused; for the absolute exclusion of all\ndoubt, the utter impossibility of suggesting any counter\nhypothesis which this assumes, is unattainable in human\naffairs. But, it is frequently said, they are to convict if\nthey have no 'reasonable doubt,' no such doubt, that is,\nas would be 'a hindrance to acting in the important affairs\nof life.' As a caution against seeking after unattainable\ncertainty, such advice may be very useful; but it need\nhardly be remarked that the certainty upon which we act in\nthe important affairs of life is no fixed standard, but varies\nexceedingly according to the nature of those affairs. The\ngreater the reward at stake, the greater the risk we are\nprepared to run, and conversely. Hardly any degree of certainty\ncan exist, upon the security of which we should not\nbe prepared to act under appropriate circumstances.[24]\n\nSome writers indeed altogether deny that any standard,\nin the common sense of the word, either is, or ought to be,\naimed at in legal proceedings. For instance, Sir J. F.\nStephen, in his work on English Criminal Law,[25] after\nnoticing and rejecting such standards as that last indicated,\ncomes to the conclusion that the only standard recognized\nby our law is that which induces juries to convict:--\"What\nis judicial proof? That which being permitted by\nlaw to be given in evidence, induces twelve men, chosen\naccording to the Jury Act, to say that, having heard it, their\nminds are satisfied of the truth of the proposition which it\naffirms. They may be prejudiced, they may be timid, they\nmay be rash, they may be ignorant; but the oath, the\nnumber, and the property qualification, are intended, as far\nas possible, to neutralize these disadvantages, and answer\nprecisely to the conditions imposed upon standards of value\nor length.\" (p. 263.)\n\nTo admit this is much about the same thing as to abandon\nsuch a standard as unattainable. Evidence which induces\na jury to convict may doubtless be a standard to me and\nothers of what we ought to consider 'reasonably certain,'\nprovided of course that the various juries are tolerably uniform\nin their conclusions. But it clearly cannot be proposed\nas a standard to the juries themselves; if their decisions are\nto be consistent and uniform, they want some external indication\nto guide them. When a man is asking, _How_ certain\nought I to feel? to give such an answer as the above is,\nsurely, merely telling him that he is to be as certain as\nhe is. If, indeed, juries composed a close profession, they\nmight, as was said above, retain a traditional standard. But\nbeing, as they are, a selection from the ordinary lay public,\ntheir own decisions in the past can hardly be held up to\nthem as a direction what they are to do in future.\n\n31. It would appear therefore that we may fairly say\nthat the English law, at any rate, definitely rejects the main\nassumption upon which the logical doctrine of modality and\nits legal counterpart are based: the assumption, namely, that\ndifferent grades of conviction can be marked off from one\nanother with sufficient accuracy for us to be able to refer\nindividual cases to their corresponding classes. And that\nwith regard to the collateral question of fixing a standard of\ncertainty, it will go no further than pronouncing, or implying,\nthat we are to be content with nothing short of, but\nneed not go beyond, 'reasonable certainty.'\n\nThis is a statement of the standard, with which the\nlogician and scientific man can easily quarrel; and they\nmay with much reason maintain that it has not the slightest\nclaim to accuracy, even if it had one to strict intelligibility.\nIf a man wishes to know whether his present degree of certainty\n_is_ reasonable, whither is he to appeal? He can\nscarcely compare his mental state with that which is experienced\nin 'the important affairs of life,' for these, as\nalready remarked, would indicate no fixed value. At the\nsame time, one cannot suppose that such an expression is\ndestitute of all signification. People would not continue to\nuse language, especially in matters of paramount importance\nand interest, without meaning something by it. We are\ndriven therefore to conclude that 'reasonable certainty' does\nin a rude sort of way represent a traditional standard to\nwhich it is attempted to adhere. As already remarked, this\nis perfectly practicable in the case of any class of professional\nmen, and therefore not altogether impossible in the case of\nthose who are often and closely brought into connection with\nsuch a class. Though it is hard to believe that any such\nexpressions, when used for purposes of ordinary life, attain\nat all near enough to any conventional standard to be worth\ndiscussion; yet in the special case of a jury, acting under\nthe direct influence of a judge, it seems quite possible that\ntheir deliberate assertion that they are 'fully convinced'\nmay reach somewhat more nearly to a tolerably fixed standard\nthan ordinary outsiders would at first think likely.\n\n32. Are there then any means by which we could\nascertain what this standard is; in other words, by which we\ncould determine what is the real worth, in respect of accuracy,\nof this 'reasonable certainty' which the juries are supposed\nto secure? In the absence of authoritative declarations\nupon the subject, the student of Logic and Probability\nwould naturally resort to two means, with a momentary\nnotice of which we will conclude this enquiry.\n\nThe first of these would aim at determining the standard\nof judicial certainty indirectly, by simply determining the\nstatistical frequency with which the decisions (say) of a jury\nwere found to be correct. This may seem to be a hopeless\ntask; and so indeed it is, but not so much on any theoretic\ninsufficiency of the determining elements as on account of\nthe numerous arbitrary assumptions which attach to most\nof the problems which deal with the probability of testimony\nand judgments. It is not necessary for this purpose that we\nshould have an infallible superior court which revised the\ndecisions of the one under consideration;[26] it is sufficient if a\nlarge number of ordinary representative cases are submitted\nto a court consisting even of exactly similar materials to the\none whose decisions we wish to test. Provided always that we\nmake the monstrous assumption that the judgments of men\nabout matters which deeply affect them are 'independent'\nin the sense in which the tosses of pence are independent,\nthen the statistics of mere agreement and disagreement will\nserve our purpose. We might be able to say, for instance,\nthat a jury of a given number, deciding by a given majority,\nwere right nine times out of ten in their verdict. Conclusions\nof this kind, in reference to the French courts, are\nwhat Poisson has attempted at the end of his great work on\nthe Probability of Judgments; though I do not suppose that\nhe attached much numerical accuracy to his results.\n\nA scarcely more hopeful means would be found by a\nreference to certain cases of legal 'presumptions.' A 'conclusive\npresumption' is defined as follows:--\"Conclusive, or\nas they are elsewhere termed imperative or absolute presumptions\nof law, are rules determining the quantity of evidence\nrequisite for the support of any particular averment\nwhich is not permitted to be overcome by any proof that the\nfact is otherwise.\"[27] A large number of such presumptions\nwill be found described in the text-books, but they seem to\nrefer to matters far too vague, for the most part, to admit of\nany reduction to statistical frequency of occurrence. It is\nindeed maintained by some authorities that any assignment\nof degree of Probability is not their present object, but that\nthey are simply meant to exclude the troublesome delays\nthat would ensue if everything were considered open to\ndoubt and question. Moreover, even if they did assign a\ndegree of certainty this would rather be an indication of\nwhat legislators or judges thought reasonable than of what\nwas so considered by the juries themselves.\n\nThere are indeed presumptions as to the time after which\na man, if not heard of, is supposed to be dead (capable of\ndisproof, of course, by his reappearance). If this time varied\nwith the age of the man in question, we should at once have\nsome such standard as we desire, for a reference to the Life\ntables would fix his probable duration of life, and so determine\nindirectly the measure of probability which satisfied\nthe law. But this is not the case; the period chosen is\nentirely irrespective of age. The nearest case in point (and\nthat does not amount to much) which I have been able to\nascertain is that of the age after which it has been presumed\nthat a woman was incapable of bearing children.\nThis was the age of 53. A certain approach to a statistical\nassignment of the chances in this case is to be found in\nQuetelet's _Physique Sociale_ (Vol. I. p. 184, note). According\nto the authorities which he there quotes it would seem that\nin about one birth in 5500 the mother was of the age of 50\nor upwards. This does not quite assign the degree of what\nmay be called the _\u00e0 priori_ chance against the occurrence of a\nbirth at that age, because the fact of having commenced a\nfamily at an early age represents some diminution of the\nprobability of continuing it into later life. But it serves to\ngive some indication of what may be called the odds against\nsuch an event.\n\nIt need not be remarked that any such clues as these to\nthe measure of judicial certainty are far too slight to be of\nany real value. They only deserve passing notice as a possible\nlogical solution of the problem in question, or rather as\nan indication of the mode in which, in theory, such a solution\nwould have to be sought, were the English law, on those\nsubjects, a perfectly consistent scheme of scientific evidence.\nThis is the mode in which one would, under those circumstances,\nattempt to extract from its proceedings an admission\nof the exact measure of that standard of certainty which it\nadopted, but which it declined openly to enunciate.\n\n\n1. _Formal Logic_, p. 232.\n\n2. This appears to be the purport of some statements in a very\n  confused passage in Whately's _Logic_ (Bk. II., ch. IV. \u00a71). \"A\n  modal proposition may be stated as a pure one by attaching the mode\n  to one of the terms, and the proposition will in all respects fall\n  under the foregoing rules;... 'It is probable that all knowledge is\n  useful;' 'probably useful' is here the predicate.\" He draws\n  apparently no such distinction as that between the true and false\n  modality referred to in the next note. What is really surprising is\n  that even Hamilton puts the two (the true and the false modality)\n  upon the same footing. \"In regard to these [the former] the case is\n  precisely the same; the mode is merely a part of the predicate.\"\n  _Logic_, I. 257.\n\n3. I allude of course to such examples as 'A killed B unjustly,' in\n  which the killing of B by A was sometimes said to be asserted not\n  simply but with a modification. (Hamilton's _Logic_, I. 256.) It is\n  obvious that the modification in such cases is by rights merely a\n  part of the predicate, there being no formal distinction between 'A\n  is the killer of B' and 'A is the unjust killer of B.' Indeed some\n  logicians who were too conservative to reject the generic name of\n  modality in this application adopted the common expedient of\n  introducing a specific distinction which did away with its meaning,\n  terming the spurious kind 'material modality' and the genuine kind\n  'formal modality'. The former included all the cases in which the\n  modification belonged by right either to the predicate or to the\n  subject; the latter was reserved for the cases in which the\n  modification affected the real conjunction of the predicate with the\n  subject. (Keckermann, _Systema Logic\u00e6_, Lib. II. ch. 3.) It was, I\n  believe, a common scholastic distinction.\n\n  For some account of the dispute as to whether the negative particle\n  was to be considered to belong to the copula or to the predicate,\n  see Hamilton's _Logic_, I. 253.\n\n4. He has also given a short discussion of the subject elsewhere\n  (_Discussions_, Ed. II. p. 702), in which a somewhat different view\n  is taken. The modes are indeed here admitted into logic, but only\n  in so far as they fall by subdivision under the relation of genus\n  and species, which is of course tantamount to their entire\n  rejection; for they then differ in no essential way from any other\n  examples of that relation.\n\n5. _Letters, Lectures and Reviews_, p. 61. Elsewhere in the review\n  (p. 45) he gives what appears to me a somewhat different decision.\n\n6. It must be remembered that this is not one of the proportional\n  propositions with which we have been concerned in previous chapters:\n  it is meant that there are _exactly_ 21 Ys, of which just 18 are X,\n  not that on the average 18 out of 21 may be so regarded.\n\n7. I consider however, as I have said further on (p. 320), that the\n  treatment in the older logics of Probable syllogisms, and Dialectic\n  syllogisms, came to somewhat the same thing as this, though they\n  looked at the matter from a different point of view, and expressed\n  it in very different language.\n\n8. The distinction is however by no means entirely neglected. Thus\n  Smiglecius, when discussing the modal affections of certainty and\n  necessity, says, \"certitudo ad cognitionem spectat: necessitas vero\n  est in re\" (_Disputationes;_ Disp. XIII., Qu\u00e6st. XII.).\n\n9. It may be remarked that Whately (_Logic_, Bk. II. ch. II. \u00a72)\n  speaks of necessary, impossible and contingent matter, without any\n  apparent suspicion that they belong entirely to an obsolete point of\n  view.\n\n10. _Formal Logic_, p. 233.\n\n11. The subject was sometimes altogether omitted, as by Wolf. He says\n  a good deal however about probable propositions and syllogisms, and,\n  like Leibnitz before him, looked forward to a \"logica probabilium\"\n  as something new and desirable. I imagine that he had been\n  influenced by the writers on Chances, as of the few who had already\n  treated that subject nearly all the most important are referred to\n  in one passage (_Philosophia Rationalis sive Logica_, \u00a7593).\n\n  Lambert stands quite apart. In this respect, as in most others where\n  mathematical conceptions and symbols are involved, his logical\n  attitude is thoroughly unconventional. See, for instance, his\n  chapter 'Von dem Wahrscheinlichen', in his _Neues Organon_.\n\n12. I cannot find the slightest authority for the statement in the\n  elaborate history of Logic by Prantl.\n\n13. \"Hi quatuor modi magnam censeri solent analogiam habere cum\n  quadruplici propositionum in quantitate et qualitate varietate\"\n  (Wallis's _Instit. Logic._ Bk. II. ch. 8).\n\n14. _Laws of Thought_, \u00a7118.\n\n15. \"Haud scio magis ne doctrinam modalium scholastici exercuerint,\n  quam ea illos vexarit. Certe usque adeo sudatum hic fuit, ut\n  dicterio locus sit datus; _De modalibus non gustabit asinus_.\"\n  Keckermann, _Syst. Log._ Bk. II. ch. 3.\n\n16. _Smiglecii Disputationes_, Ingolstadt, 1618.\n\n  See also Prantl's _Geschichte der Logik_ (under _Occam_ and\n  _Buridan_) for accounts of the excessive complication which the\n  subtlety of those learned schoolmen evolved out of such suitable\n  materials.\n\n17. Translation by T. M. Lindsay, p. 439.\n\n18. \"The \u03b5\u1f30\u03ba\u00f2\u03c2 and \u03c3\u03b7\u03bc\u03b5\u1fd6\u03bf\u03bd themselves are propositions; the former\n  stating a _general probability_, the latter a fact, which is known\n  to be an indication, more or less certain, of the truth of some\n  further statement, whether of a single fact, or of a general\n  belief. The former is a general proposition, nearly, though not\n  quite, universal; as 'most men who envy hate'; the latter is a\n  _singular_ proposition, which however is not regarded as a sign,\n  except relatively to some other proposition, which it is supposed\n  may by inferred from it.\" (Mansel's Aldrich; Appendix F, where an\n  account will be found of the Aristotelian enthymeme, and dialectic\n  syllogism. Also, of course, Grote's Aristotle, _Topics_ and\n  elsewhere.)\n\n19. \"Nam in hoc etiam differt demonstratio, sen demonstrativa\n  argumentatio, \u00e0 probabili, quia in ill\u00e2 tam conclusio quam pr\u00e6miss\u00e6\n  necessari\u00e6 sunt; in probabili autem argumentatione sicut conclusio\n  ut probabilis infertur ita pr\u00e6miss\u00e6 ut probabiles afferuntur\"\n  (Crackanthorpe, Bk. V., Ch. 1); almost the words with which De\n  Morgan distinguishes between logic and probability in a passage\n  already cited (see Ch. VI. \u00a73).\n\n  Perhaps it was a development of some such view as this that Leibnitz\n  looked forward to. \"J'ai dit plus d'une fois qu'il faudrait une\n  nouvelle esp\u00e8ce de Logique, qui traiteroit des degr\u00e9s de\n  Probabilit\u00e9, puisqu'Aristote dans ses Topiques n'a rien moins fait\n  que cela\" (_Nouveaux essais_, Lib. IV. ch. XVI). It is possible,\n  indeed, that he had in his mind more what we now understand by the\n  mathematical theory of Probability, but in the infancy of a science\n  it is of course hard to say whether any particular subject is\n  definitely contemplated or not. Leibnitz (as Todhunter has shown in\n  his history) took the greatest interest in such chance problems as\n  had yet been discussed.\n\n20. By _loci_ were understood certain general classes of\n  premises. They stood, in fact, to the major premise in somewhat the\n  same relation that the Category or Predicament did to the\n  term. Crackanthorpe says of them, \"sed duci a _loco probabiliter\n  arguendi_, hoc vere proprium est Argumentationis probabilis; et in\n  hoc a Demonstratione differt, quia Demonstrator utitur solummodo\n  quatuor Locis eisque necessariis.... Pr\u00e6ter hos autem, ex quibus\n  quoque probabiliter arguere licet, sunt multo plures Loci arguendi\n  probabiliter; ut a Genere, a Specie, ab Adjuncto, ab Oppositis, et\n  similia\" (_Logica_, Lib. V., ch. II.).\n\n21. Stephen's _General View of the Criminal Law of England_, p. 241.\n\n22. _Rationale of Judicial Evidence_; Bk. I. ch. VI.\n\n23. Though this is claimed by some Kantian logicians;--Nie darf an\n  einem angeblichen Verbrecher die gesetzliche Strafe vollzogen\n  werden, bevor er nicht selbst das Verbrechen eingestanden. Denn wenn\n  auch alle Zeugnisse und die \u00fcbrigen Anzeigen wider ihn w\u00e4ren, so\n  bleibt doch das Gegentheil immer m\u00f6glich\" (Krug, _Denklehre_, \u00a7131).\n\n24. As Mr C. J. Monro puts it: \"Suppose that a man is suspected of\n  murdering his daughter. Evidence which would not convict him before\n  an ordinary jury might make a grand jury find a true bill; evidence\n  which would not do this might make a coroner's jury bring in a\n  verdict against him; evidence which would not do this would very\n  often prevent a Chancery judge from appointing the man guardian to a\n  ward of the court; evidence which would not affect the judge's mind\n  might make a father think twice on his death-bed before he appointed\n  the man guardian to _his_ daughter.\"\n\n25. The portions of this work which treat of the nature of proof in\n  general, and of judicial proof in particular, are well worth reading\n  by every logical student. It appears to me, however, that the author\n  goes much too far in the direction of regarding proof as subjective,\n  that is as what _does_ satisfy people, rather than as what _should_\n  satisfy them. He compares the legislative standard of certainty with\n  that of value; this latter is declared to be a certain weight of\n  gold, irrespective of the rarity or commonness of that metal. So\n  with certainty; if people grow more credulous the intrinsic value of\n  the standard will vary.\n\n26. The question will be more fully discussed in a future chapter, but\n  a few words may be inserted here by way of indication. Reduce the\n  case to the simplest possible elements by supposing only two judges\n  or courts, of the same average correctness of decision. Let this be\n  indicated by x. Then the chance of their agreeing is\n  x^{2} + (1 - x)^{2}, for they agree if both are right or both wrong.\n  If the statistical frequency of this agreement is known, that is, the\n  frequency with which the first judgment is confirmed by the second,\n  we have the means of determining x.\n\n27. Taylor on Evidence: the latter part of the extract does not seem\n  very clear.\n\n\n\n\nCHAPTER XIV.\n\n\n_FALLACIES._\n\n1. In works on Logic a chapter is generally devoted\nto the discussion of Fallacies, that is, to the description\nand classification of the different ways in which the rules\nof Logic may be transgressed. The analogy of Probability\nto Logic is sufficiently close to make it advisable to adopt\nthe same plan here. In describing his own opinions an\nauthor is, of course, perpetually obliged to describe and\ncriticise those of others which he considers erroneous. But\nsome of the most widely spread errors find no supporters\nworth mentioning, and exist only in vague popular misapprehension.\nIt will be found the best arrangement, therefore,\nat the risk of occasional repetition, to collect a few of\nthe errors that occur most frequently, and as far as possible\nto trace them to their sources; but it will hardly be worth\nthe trouble to attempt any regular system of arrangement\nand classification. We shall mainly confine ourselves, in\naccordance with the special province of this work, to problems\nwhich involve questions of logical interest, or to those\nwhich refer to the application of Probability to moral and\nsocial science. We shall avoid the discussion of isolated\nproblems in games of chance and skill except when some\nerror of principle seems to be involved in them.\n\n2. (I.) One of the most fertile sources of error and\nconfusion upon the subject has been already several times\nalluded to, and in part discussed in a previous chapter.\nThis consists in choosing the class to which to refer an\nevent, and therefore judging of the rarity of the event and\nthe consequent improbability of foretelling it, _after it has\nhappened_, and then transferring the impressions we experience\nto a supposed contemplation of the event beforehand.\nThe process in itself is perfectly legitimate (however unnecessary\nit may be), since time does not in strictness enter\nat all into questions of Probability. No error therefore\nneed arise in this way, if we were careful as to the class\nwhich we thus selected; but such carefulness is often neglected.\n\nAn illustration may afford help here. A man once\npointed to a small target chalked upon a door, the target\nhaving a bullet hole through the centre of it, and surprised\nsome spectators by declaring that he had fired that shot\nfrom an old fowling-piece at a distance of a hundred yards,\nHis statement was true enough, but he suppressed a rather\nimportant fact. The shot had really been aimed in a general\nway at the barn-door, and had hit it; the target was afterwards\nchalked round the spot where the bullet struck. A\ndeception analogous to this is, I think, often practised unconsciously\nin other matters. We judge of events on a similar\nprinciple, feeling and expressing surprise in an equally unreasonable\nway, and deciding as to their occurrence on\ngrounds which are really merely a subsequent adjunct of our\nown. Butler's remarks about 'the story of C\u00e6sar,' discussed\nalready in the twelfth chapter, are of this character. He\nselects a series of events from history, and then imagines a\nperson guessing them correctly who at the time had not the\nhistory before him. As I have already pointed out, it is one\nthing to be unlikely to guess an event rightly without\nspecific evidence; it is another and very different thing to\nappreciate the truth of a story which is founded partly or\nentirely upon evidence. But it is a great mistake to transfer\nto one of these ways of viewing the matter the mental impressions\nwhich properly belong to the other. It is like\ndrawing the target afterwards, and then being surprised to\nfind that the shot lies in the centre of it.\n\n3. One aspect of this fallacy has been already discussed,\nbut it will serve to clear up difficulties which are\noften felt upon the subject if we reexamine the question\nunder a somewhat more general form.\n\nIn the class of examples under discussion we are generally\npresented with an individual which is not indeed definitely\nreferred to a class, but in regard to which we have no great\ndifficulty in choosing the appropriate class. Now suppose\nwe were contemplating such an event as the throwing of\nsixes with a pair of dice four times running. Such a throw\nwould be termed a very unlikely event, as the odds against\nits happening would be 36 \u00d7 36 \u00d7 36 \u00d7 36 - 1 to 1 or 1679615\nto 1. The meaning of these phrases, as has been abundantly\npointed out, is simply that the event in question occurs very\nrarely; that, stated with numerical accuracy, it occurs once in\n1679616 times.\n\n4. But now let us make the assumption that the\nthrow has actually occurred; let us put ourselves into the\nposition of contemplating sixes four times running when it is\nknown or reported that this throw has happened. The same\nphrase, namely that the event is a very unlikely one, will\noften be used in relation to it, but we shall find that this\nphrase may be employed to indicate, on one occasion or\nanother, extremely different meanings.\n\n(1) There is, firstly, the most correct meaning. The\nevent, it is true, has happened, and we know what it is, and\ntherefore, we have not really any occasion to resort to the\nrules of Probability; but we can nevertheless conceive ourselves\nas being in the position of a person who does not\nknow, and who has only Probability to appeal to. By calling\nthe chances 1679615 to 1 against the throw we then mean\nto imply the fact, that inasmuch as such a throw occurs only\nonce in 1679616 times, our guess, were we to guess, would\nbe correct only once in the same number of times; provided,\nthat is, that it is a fair guess, based simply on these statistical\ngrounds.\n\n5. (2) But there is a second and very different conception\nsometimes introduced, especially when the event in\nquestion is supposed to be known, not as above by the evidence\nof our experience, but by the report of a witness. We\nmay then mean by the 'chances against the event' (as was\npointed out in Chapter XII.) not the proportional number of\ntimes we should be right in guessing the event, but the\nproportional number of times the witness will be right in\nreporting it. The bases of our inference are here shifted\non to new ground. In the former case the statistics were\nthe throws and their respective frequency, now they are the\nwitnesses' statements and their respective truthfulness.\n\n6. (3) But there is yet another meaning sometimes\nintended to be conveyed when persons talk of the chances\nagainst such an event as the throw in question. They may\nmean--not, Here is an event, how often should I have\nguessed it?--nor, Here is a report, how often will it be\ncorrect?--but something different from either, namely, Here\nis an event, how often will it be found to be produced by\nsome one particular kind of cause?\n\nWhen, for example, a man hears of dice giving the same\nthrow several times running, and speaks of this as very\nextraordinary, we shall often find that he is not merely\nthinking of the improbability of his guess being right, or of\nthe report being true, but, that along with this, he is introducing\nthe question of the throw having been produced by\nfair dice. There is, of course, no reason whatever why such\na question as this should not also be referred to Probability,\nprovided always that we could find the appropriate statistics\nby which to judge. These statistics would be composed, not\nof throws of the particular dice, nor of reports of the particular\nwitness, but of the occasions on which such a throw as\nthe one in question respectively had, and had not, been\nproduced fairly. The objection to entering upon this view\nof the question would be that no such statistics are obtainable,\nand that if they were, we should prefer to form our\nopinion (on principles to be described in Chapter XVI.) from\nthe special circumstances of the case rather than from an\nappeal to the average.\n\n7. The reader will easily be able to supply examples\nin illustration of the distinctions just given; we will briefly\nexamine but one. I hide a banknote in a certain book in a\nlarge library, and leave the room. A person tells me that,\nafter I went out, a stranger came in, walked straight up to\nthat particular book, and took it away with him. Many\npeople on hearing this account would reply, How extremely\nimprobable! On analysing the phrase, I think we shall\nfind that certainly two, and possibly all three, of the above\nmeanings might be involved in this exclamation. (1) What\nmay be meant is this,--Assuming that the report is true,\nand the stranger innocent, a rare event has occurred. Many\nbooks might have been thus taken without that particular\none being selected. I should not therefore have expected\nthe event, and when it has happened I am surprised. Now\na man has a perfect right to be surprised, but he has no\nlogical right (so long as we confine ourselves to this view) to\nmake his surprise a ground for disbelieving the event. To\ndo this is to fall into the fallacy described at the commencement\nof this chapter. The fact of my not having been likely\nto have guessed a thing beforehand is no reason in itself for\ndoubting it when I am informed of it. (2) Or I may stop\nshort of the events reported, and apply the rules of Probability\nto the report itself. If so, what I mean is that such a\nstory as this now before me is of a kind very generally false,\nand that I cannot therefore attach much credit to it now.\n(3) Or I may accept the truth of the report, but doubt the\nfact of the stranger having taken the book at random. If\nso, what I mean is, that of men who take books in the way\ndescribed, only a small proportion will be found to have\ntaken them really at random; the majority will do so because\nthey had by some means ascertained, or come to suspect,\nwhat there was inside the book.\n\nEach of the above three meanings is a possible and a\nlegitimate meaning. The only requisite is that we should be\ncareful to ascertain which of them is present to the mind, so\nas to select the appropriate statistics. The first makes in\nitself the most legitimate use of Probability; the drawback\nbeing that at the time in question the functions of Probability\nare superseded by the event being otherwise known.\nThe second or third, therefore, is the more likely meaning to\nbe present to the mind, for in these cases Probability, if it\ncould be practically made use of, would, at the time in\nquestion, be a means of drawing really important inferences.\nThe drawbacks are the difficulty of finding such statistics,\nand the extreme disturbing influence upon these statistics of\nthe circumstances of the special case.\n\n8. (II.) Closely connected with the tendency just\nmentioned is that which prompts us to confound a true\nchance selection with one which is more or less picked.\nWhen we are dealing with familiar objects in a concrete\nway, especially when the greater rarity corresponds to superiority\nof quality, almost every one has learnt to recognize\nthe distinction. No one, for instance, on observing a fine\nbody of troops in a foreign town, but would be prompted to\nask whether they came from an average regiment or from\none that was picked. When however the distinction refers\nto unfamiliar objects, and especially when only comparative\nrarity seems to be involved, the fallacy may assume a rather\nsubtle and misleading form, and seems to deserve special\nnotice by the consideration of a few examples.\n\nSometimes the result is not so much an actual fallacy as\na slight misreckoning of the order of probability of the event\nunder consideration. For instance, in the Pyramid question,\nwe saw that it made some difference whether we considered\nthat \u03c0 alone was to be taken into account or whether we\nput this constant into a class with a small number of other\nsimilar ones. In deciding, however, whether or not there is\nanything remarkable in the actual falling short of the\nrepresentation of the number 7 in the evaluation of \u03c0\n(v. p. 248) the whole question turns upon considerations of\nthis kind. The only enquiry raised is whether there is anything\nremarkable in this departure from the mean, and the\nanswer depends upon whether we suppose that we are referring\nto a predetermined digit, or to whatever digit of the\nten happens to be most above or below the average. Or,\ntake the case raised by Cournot (_Exposition de la Th\u00e9orie\ndes Chances_, \u00a7\u00a7102, 114), that a certain deviation from the\nmean in the case of Departmental returns of the proportion\nbetween male and female births is significant and indicative\nof a difference in kind, provided that we select at random a\nsingle French Department; but that the same deviation may\nbe accidental if it is the maximum of the respective returns\nfor several Departments.[1] The answer may be given one\nway or the other according as we bear this consideration in\nmind.\n\n9. We are peculiarly liable to be misled in this way\nwhen we are endeavouring to determine the cause of some\nphenomenon, by mere statistics, in entire ignorance as to the\ndirection in which the cause should be expected. In such\ncases an ingenious person who chooses to look about over a\nlarge field can never fail to hit upon an explanation which is\nplausible in the sense that it fits in with the hitherto observed\nfacts. With a tithe of the trouble which Mr Piazzi\nSmyth expended upon the measurement of the great pyramid,\nI think I would undertake to find plausible intimations of\nseveral of the important constants and standards which he\ndiscovered there, in the dimensions of the desk at which I am\nwriting. The oddest instance of this sort of conclusion is\nperhaps to be found in the researches of a writer who has\ndiscovered[2] that there is a connection of a striking kind\nbetween the respective successes of the Oxford and the\nCambridge boat in the annual race, and the greater and less\nfrequency of sun-spots.\n\nOf course our usual practical resource in such cases is to\nmake appeal to our previous knowledge of the subject in\nquestion, which enables us to reject as absurd a great number\nof hypotheses which can nevertheless make a fair show when\nthey are allowed to rest upon a limited amount of adroitly\nselected instances. But it must be remembered that if any\ntheory chooses to appeal to statistics, to statistics it must be\nsuffered to go for judgment. Even the boat race theory\ncould be established (if sound) on this ground alone. That\nis, if it really could be shown that experience in the long run\nconfirmed the preponderance of successes on one side or the\nother according to the relative frequency of the sun-spots,\nwe should have to accept the fact that the two classes of\nevents were not really independent. One of the two, whichever\nit may be, must be suspected of causing or influencing\nthe other; or both must be caused or influenced by some\ncommon circumstances.\n\n10. (III.) The fallacy described at the commencement\nof this chapter arose from determining to judge of an observed\nor reported event by the rules of Probability, but\nemploying a wrong set of statistics in the process of judging.\nAnother fallacy, closely connected with this, arises from the\npractice of taking some only of the characteristics of such an\nevent, and arbitrarily confining to these the appeal to Probability.\nSuppose I toss up twelve pence and find that eleven\nof them give heads. Many persons on witnessing such an occurrence\nwould experience a feeling which they would express by\nthe remark, How near that was to getting all heads! And if\nany thing very important were staked on the throw they\nwould be much excited at the occurrence. But in what\nsense were we near to twelve? There is a not uncommon\nerror, I apprehend, which consists in unconsciously regarding\nthe eleven heads as a thing which is already somehow\nsecured, so that one might as it were keep them, and then\ntake our chance for securing the remaining one. The eleven\nare mentally set aside, looked upon as certain (for they have\nalready happened), and we then introduce the notion of\nchance merely for the twelfth. But this twelfth, having\nalso happened, has no better claim to such a distinction than\nany of the others. If we will introduce the notion of chance\nin the case of the one that gave tail we must do the same in\nthe case of all the others as well. In other words, if the\ntosser be dissatisfied at the appearance of the one tail, and\nwish to cancel it and try his luck again, he must toss up the\nwhole lot of pence again fairly together. In this case, of\ncourse, so far from his having a better prospect for the next\nthrow he may think himself in very good luck if he makes\nagain as good a throw as the one he rejected. What he is\ndoing is confounding this case with that in which the throws\nare really _successive_. If eleven heads have been tossed up in\nturn, we are of course within an even chance of getting a\ntwelfth; but the circumstances are quite different in the\ninstance proposed.\n\n11. In the above example the error is transparent.\nBut in forming a judgment upon matters of greater complexity\nthan dice and pence, especially in the case of what are\ncalled 'narrow escapes,' a mistake of an analogous kind is, I\napprehend, far from uncommon. A person, for example, who\nhas just experienced a narrow escape will often be filled\nwith surprise and anxiety amounting almost to terror. The\nevent being past, these feelings are, at the time, in strictness\ninappropriate. If, as is quite possible, they are merely instinctive,\nor the result of association, they do not fall within\nthe province of any kind of Logic. If, however, as seems\nmore likely, they partially arise from a supposed transference\nof ourselves into that point of past time at which the event\nwas just about to happen, and the production by imagination\nof the feelings we should then expect to experience,\nthis process partakes of the nature of an inference, and can\nbe right or wrong. In other words, the alarm may be proportionate\nor disproportionate to the amount of danger that\nmight fairly have been reckoned upon in such a hypothetical\nanticipation. If the supposed transfer were completely\ncarried out, there would be no fallacy; but it is often very\nincompletely done, some of the component parts of the event\nbeing supposed to be determined or 'arranged' (to use a\nsporting phrase) in the form in which we now know that\nthey actually have happened, and only the remaining ones\nbeing fairly contemplated as future chances.\n\nA man, for example, is out with a friend, whose rifle goes\noff by accident, and the bullet passes through his hat. He\ntrembles with anxiety at thinking what might have happened,\nand perhaps remarks, 'How very near I was to being\nkilled!' Now we may safely assume that he means something\nmore than that a shot passed very close to him. He\nhas some vague idea that, as he would probably say, 'his\nchance of being killed then was very great.' His surprise\nand terror may be in great part physical and instinctive,\narising simply from the knowledge that the shot had passed\nvery near him. But his mental state may be analysed, and\nwe shall then most likely find, at bottom, a fallacy of the\nkind described above. To speak or think of chance in connection\nwith the incident, is to refer the particular incident\nto a class of incidents of a similar character, and then to consider\nthe comparative frequency with which the contemplated\nresult ensues. Now the series which we may suppose\nto be most naturally selected in this case is one composed of\nshooting excursions with his friend; up to this point the\nproceedings are assumed to be designed, beyond it only,\nin the subsequent event, was there accident. Once in a\nthousand times perhaps on such occasions the gun will go\noff accidentally; one in a thousand only of those discharges\nwill be directed near his friend's head. If we will make the\naccident a matter of Probability, we ought by rights in this\nway (to adopt the language of the first example), to 'toss up\nagain' fairly. But we do not do this; we seem to assume for\ncertain that the shot goes within an inch of our heads, detach\nthat from the notion of chance at all, and then begin to\nintroduce this notion again for possible deflections from that\nsaving inch.\n\n12. (IV.) We will now notice a fallacy connected with\nthe subjects of betting and gambling. Many or most of the\npopular misapprehensions on this subject imply such utter\nignorance and confusion as to the foundations of the science\nthat it would be needless to discuss them here. The following\nhowever is of a far more plausible kind, and has been a\nsource of perplexity to persons of considerable acuteness.\n\nThe case, put into the simplest form, is as follows.[3]\nSuppose that a person A is playing against B, B being\neither another individual or a group of individuals, say a\ngambling bank. They begin by tossing for a shilling, and\nA maintains that he is in possession of a device which will\ninsure his winning. If he does win on the first occasion he\nhas clearly gained his point so far. If he loses, he stakes\nnext time two shillings instead of one. The result of course\nis that if he wins on the second occasion he replaces his\nformer loss, and is left with one shilling profit as well. So\nhe goes on, doubling his stake after every loss, with the\nobvious result that on the first occasion of success he makes\ngood all his previous losses, and is left with a shilling over.\nBut such an occasion must come sooner or later, by the\nassumptions of chance on which the game is founded. Hence\nit follows that he can insure, sooner or later, being left a\nfinal winner. Moreover he may win to any amount; firstly\nfrom the obvious consideration that he might make his\ninitial stake as large as he pleased, a hundred pounds, for\ninstance, instead of a shilling; and secondly, because what\nhe has done once he may do again. He may put his shilling\nby, and have a second spell of play, long or short as the case\nmay be, with the same termination to it. Accordingly by\nmere persistency he may accumulate any sum of money he\npleases, in apparent defiance of all that is meant by luck.\n\n13. I have classed this opinion among fallacies, as the\npresent is the most convenient opportunity of discussing it,\nthough in strictness it should rather be termed a paradox,\nsince the conclusion is perfectly sound. The only fallacy\nconsists in regarding such a way of obtaining the result as\nmysterious. On the contrary, there is nothing more easy\nthan to insure ultimate success under the given conditions.\nThe point is worth enquiry, from the principles it involves,\nand because the answers commonly given do not quite meet\nthe difficulty. It is sometimes urged, for instance, that no\nbank would or does allow the speculator to choose at will the\namount of his stake, but puts a limit to the amount for\nwhich it will consent to play. This is quite true, but is of\ncourse no answer to the hypothetical enquiry before us, which\nassumes that such a state of things _is_ allowed. Again, it has\nbeen urged that the possibility in question turns entirely\nupon the fact that credit must be supposed to be given, for\notherwise the fortune of the player may not hold out until\nhis turn of luck arrives:--that, in fact, sooner or later, if he\ngoes on long enough, his fortune will not hold out long\nenough, and all his gains will be swept away. It is quite\ntrue that credit is a _condition_ of success, but it is in no sense\nthe cause. We may suppose both parties to agree at the\noutset that there shall be no payments until the game be\nended, A having the right to decide when it shall be considered\nto be ended. It still remains true that whereas in\nordinary gambling, i.e. with fixed or haphazard stakes, A could\nnot ensure winning eventually to any extent, he can\ndo so if he adopt such a scheme as the one in question. And\nthis is the state of things which seems to call for explanation.\n\n14. What causes perplexity here is the supposed fact\nthat in some mysterious way certainty has been conjured out\nof uncertainty; that in a game where the detailed events are\nutterly inscrutable, and where the average, by supposition,\nshows no preference for either side, one party is nevertheless\nsucceeding somehow in steadily drawing the luck his own\nway. It looks as if it were a parallel case with that of a\nman who should succeed by some device in permanently\nsecuring more than half of the tosses with a penny which\nwas nevertheless to be regarded as a perfectly fair one.\n\nThis is quite a mistake. The real fact is that A does\nnot expose his gains to chance at all; all that he so exposes\nis the number of times he has to wait until he gains. Put\nsuch a case as this. I offer to give a man any sum of money\nhe chooses to mention provided he will at once give it back\nagain to me with one pound more. It does not need much\nacuteness to see that it is a matter of indifference to me\nwhether he chooses to mention one pound, or ten, or a\nhundred. Now suppose that instead of leaving it to his\nchoice which of these sums is to be selected each time, the\ntwo parties agree to leave it to chance. Let them, for\ninstance, draw a number out of a bag each time, and let that\nbe the sum which A gives to B under the prescribed conditions.\nThe case is not altered. A still gains his pound each\ntime, for the introduction of the element of chance has not\nin any way touched this. All that it does is to make this\npound the result of an uncertain subtraction, sometimes 10\n_minus_ 9, sometimes 50 _minus_ 49, and so on. It is these\nnumbers only, not their difference, which he submits to luck,\nand this is of no consequence whatever.\n\nTo suggest to any individual or company that they\nshould consent to go on playing upon such terms as these\nwould be too barefaced a proposal. And yet the case in\nquestion is identical in principle, and almost identical in\nform, with this. To offer to give a man any sum he likes to\nname provided he gives you back again that same sum _plus_\none, and to offer him any number of terms he pleases of the\nseries 1, 2, 4, 8, 16, &c., provided you have the next term of\nthe set, are equivalent. The only difference is that in the\nlatter case the result is attained with somewhat more of\narithmetical parade. Similarly equivalent are the processes\nin case we prefer to leave it to chance, instead of to choice,\nto decide what sum or what number of terms shall be fixed\nupon. This latter is what is really done in the case in\nquestion. A man who consents to go on doubling his stake\nevery time he wins, is leaving nothing else to chance than\nthe determination of the particular number of terms of such\na geometrical series which shall be allowed to pass before he\nstops.\n\n15. It may be added that there is no special virtue in\nthe particular series in question, viz. that in accordance with\nwhich the stake is doubled each time. All that is needed is\nthat the last term of the series should more than balance all\nthe preceding ones. Any other series which increased faster\nthan this geometrical one, would answer the purpose as well\nor better. Nor is it necessary, again, that the game should\nbe an even or 'fair' one. Chance, be it remembered, affects\nnothing here but the number of terms to which the series\nattains on each occasion, its final result being always arithmetically\nfixed. When a penny is tossed up it is only on\none of every two occasions that the series runs to more than\ntwo terms, and so his fixed gains come in pretty regularly.\nBut unless he was playing for a limited time only, it would\nnot affect him if the series ran to two hundred terms; it\nwould merely take him somewhat longer to win his stakes.\nA man might safely, for instance, continue to lay an _even_\nbet that he would get the single prize in a lottery of a thousand\ntickets, provided he thus doubled, or more than doubled,\nhis stake each time, and unlimited credit was given.\n\n16. So regarded, the problem is simple enough, but\nthere are two points in it to which attention may conveniently\nbe directed.\n\nIn the first place, it serves very pointedly to remind us of\nthe distinction between a series of events (in this case the\ntosses of the penny) which really are subjects of chance, and\nour conduct founded upon these events, which may or may\nnot be so subject.[4] It is quite possible that this latter may\nbe so contrived as to be in many respects a matter of absolute\ncertainty,--a consideration, I presume, familiar enough\nto professional betting men. Why is the ordinary way of\nbetting on the throws of a penny fair to both parties? Because\na 'fair' series is 'fairly' treated. The heads and tails\noccur at random, but on an average equally often, and the\nstakes are either fixed or also arranged at random. If a man\nbacks heads every time for the same amount, he will of\ncourse in the long run neither win nor lose. Neither will he\nif he varies the stake every time, provided he does not vary\nit in such a way as to make its amount dependent on the\nfact of his having won or lost the time before. But he\nmay, if he pleases, and the other party consents, so arrange\nhis stakes (as in the case in question) that Chance, if one\nmight so express it, does not get a fair chance. Here the\nhuman elements of choice and design have been so brought\nto bear upon a series of events which, regarded by themselves,\nexhibit nothing but the physical characteristics of\nchance, that the latter elements disappear, and we get a\nresult which is arithmetically certain. Other analogous\ninstances might be suggested, but the one before us has the\nmerit of most ingeniously disguising the actual process.\n\n17. The meaning of the remark just made will be\nbetter seen by a comparison with the following case. It has\nbeen attempted[5] to explain the preponderance of male births\nover female by assuming that the chances of the two are\nequal, but that the general desire to have a male heir tends\nto induce many unions to persist until the occurrence of this\nevent, and no longer. It is supposed that in this way there\nwould be a slight preponderance of families which consisted\nof one son only, or of two sons and one daughter, and so forth.\n\nThis is quite fallacious (as had been noticed by Laplace,\nin his _Essai_); and there could not be a better instance\nchosen than this to show just what we can do and what we\ncannot do in the way of altering the luck in a real chance-succession\nof events. To suppose that the number of actual\nbirths could be influenced in the way in question is exactly\nthe same thing as to suppose that a number of gamblers\ncould increase the ratio of heads to tails, to something over\none-half, by each handing the coin to his neighbour as soon\nas he had thrown a head: that they have only to leave off as\nsoon as head has appeared; an absurdity which we need not\npause to explain at this stage. The essential point about\nthe 'Martingale' is that, whereas the occurrence of the\nevents on which the stakes are laid is unaffected, the stakes\nthemselves can be so adjusted as to make the luck swing one\nway.\n\n18. In the second place, this example brings before us\nwhat has had to be so often mentioned already, namely, that\nthe series of Probability are in strictness supposed to be\ninterminable. If therefore we allow either party to call\nupon us to stop, especially at a point which just happens to\nsuit him, we may get results decidedly opposed to the\nintegrity of the theory. In the case before us it is a necessary\nstipulation for A that he may be allowed to leave off\nwhen he wishes, that is at one of the points at which the\nthrow is in his favour. Without this stipulation he may be\nleft a loser to any amount.\n\nIntroduce the supposition that one party may arbitrarily\ncall for a stoppage when it suits him and refuse to permit it\nsooner, and almost any system of what would be otherwise fair\nplay may be converted into a very one-sided arrangement.\nIndeed, in the case in question, A need not adopt this device\nof doubling the stakes every time he loses. He may play\nwith a fixed stake, and nevertheless insure that _one_ party\nshall win any assigned sum, assuming that the game is even\nand that he is permitted to play on credit.\n\n19. (V.) A common mistake is to assume that a very\nunlikely thing will not happen at all. It is a mistake which,\nwhen thus stated in words, is too obvious to be committed,\nfor the meaning of an unlikely thing is one that happens at\nrare intervals; if it were not assumed that the event would\nhappen sometimes it would not be called unlikely, but impossible.\nThis is an error which could scarcely occur except\nin vague popular misapprehension, and is so abundantly refuted\nin works on Probability, that it need only be touched\nupon briefly here. It follows of course, from our definition\nof Probability, that to speak of a very rare combination of\nevents as one that is 'sure never to happen,' is to use language\nincorrectly. Such a phrase may pass current as a\nloose popular exaggeration, but in strictness it involves a\ncontradiction. The truth about such rare events cannot be\nbetter described than in the following quotation from De Morgan:[6]--\n\n\"It is said that no person ever _does_ arrive at such extremely\nimprobable cases as the one just cited [drawing the\nsame ball five times running out of a bag containing twenty\nballs]. That a given individual should never throw an ace\ntwelve times running on a single die, is by far the most\nlikely; indeed, so remote are the chances of such an event\nin any twelve trials (more than 2,000,000,000 to 1 against it)\nthat it is unlikely the experience of any given country, in\nany given century, should furnish it. But let us stop for a\nmoment, and ask ourselves to what this argument applies.\nA person who rarely touches dice will hardly believe that\ndoublets sometimes occur three times running; one who handles\nthem frequently knows that such is sometimes the fact.\nEvery very practised user of those implements has seen still\nrarer sequences. Now suppose that a society of persons had\nthrown the dice so often as to secure a run of six aces observed\nand recorded, the preceding argument would still be\nused against twelve. And if another society had practised\nlong enough to see twelve aces following each other, they\nmight still employ the same method of doubting as to a run\nof twenty-four; and so on, _ad infinitum_. The power of imagining\ncases which contain long combinations so much exceeds\nthat of exhibiting and arranging them, that it is easy\nto assign a telegraph which should make a separate signal\nfor every grain of sand in a globe as large as the visible universe,\nupon the hypothesis of the most space-penetrating\nastronomer. The fallacy of the preceding objection lies in\nsupposing events in number beyond our experience, composed\nentirely of sequences such as fall within our experience. It\nmakes the past necessarily contain the whole, as to the quality\nof its components; and judges by samples. Now the\nleast cautious buyer of grain requires to examine a handful\nbefore he judges of a bushel, and a bushel before he judges\nof a load. But relatively to such enormous numbers of combinations\nas are frequently proposed, our experience does not\ndeserve the title of a handful as compared with a bushel, or\neven of a single grain.\"\n\n20. The origin of this inveterate mistake is not difficult\nto be accounted for. It arises, no doubt, from the exigencies\nof our practical life. No man can bear in mind\nevery contingency to which he may be exposed. If therefore\nwe are ever to do anything at all in the world, a large number\nof the rarer contingencies must be left entirely out of\naccount. And the necessity of this oblivion is strengthened\nby the shortness of our life. Mathematically speaking, it\nwould be said to be certain that any one who lives long\nenough will be bitten by a mad dog, for the event is not an\nimpossible, but only an improbable one, and must therefore\ncome to pass in time. But this and an indefinite number\nof other disagreeable contingencies have on most occasions\nto be entirely ignored in practice, and thence they come\nalmost necessarily to drop equally out of our thought and\nexpectation. And when the event is one in itself of no importance,\nlike a rare throw of the dice, a great effort of\nimagination may be required, on the part of persons not accustomed\nto abstract mathematical calculation, to enable\nthem to realize the throw as being even possible.\n\nAttempts have sometimes been made to estimate what\nextremity of unlikelihood ought to be considered as equivalent\nto this practical zero point of belief. In so far as\nsuch attempts are carried out by logicians, or by those who\nare unwilling to resort to mathematical valuation of chances,\nthey must be regarded as merely a special form of the modal\ndifficulties discussed in the last chapter, and need not therefore\nbe reconsidered here; but a word or two may be added\nconcerning the views of some who have looked at the matter\nfrom the mathematician's point of view.\n\nThe principal of these is perhaps Buffon. He has arrived\nat the estimate (_Arithm\u00e9tique Morale_ \u00a7VIII.) that this\npractical zero is equivalent to a chance of 1/10,000. The\ngrounds for selecting this fraction are found in the fact that,\naccording to the tables of mortality accessible to him, it\nrepresents the chance of a man of 56 dying in the course of\nthe next day. But since no man under common circumstances\ntakes the chance into the slightest consideration, it\nfollows that it is practically estimated as having no value.\n\nIt is obvious that this result is almost entirely arbitrary,\nand in fact his reasons cannot be regarded as anything more\nthan a slender justification from experience for adopting a\nconveniently simple fraction; a justification however which\nwould apparently have been equally available in the case of\nany other fractions lying within wide limits of the one\nselected.[7]\n\n21. There is one particular form of this error, which,\nfrom the importance occasionally attached to it, deserves\nperhaps more special examination. As stated above, there\ncan be no doubt that, however unlikely an event may be, if\nwe (loosely speaking) vary the circumstances sufficiently, or\nif, in other words, we keep on trying long enough, we shall\nmeet with such an event at last. If we toss up a pair of\ndice a few times we shall get doublets; if we try longer with\nthree we shall get triplets, and so on. However unusual the\nevent may be, even were it sixes a thousand times running,\nit will come some time or other if we have only patience and\nvitality enough. Now apply this result to the letters of the\nalphabet. Suppose that one letter at a time is drawn from\na bag which contains them all, and is then replaced. If the\nletters were written down one after another as they occurred,\nit would commonly be expected that they would be found to\nmake mere nonsense, and would never arrange themselves\ninto the words of any language known to men. No more\nthey would in general, but it is a commonly accepted result\nof the theory, and one which we may assume the reader to\nbe ready to admit without further discussion, that, if the\nprocess were continued long enough, words making sense\nwould appear; nay more, that any book we chose to mention,--Milton's\n_Paradise Lost_ or the plays of Shakespeare,\nfor example,--would be produced in this way at last. It\nwould take more days than we have space in this volume to\nrepresent in figures, to make tolerably certain of obtaining\nthe former of these works by thus drawing letters out of a\nbag, but the desired result would be obtained at length.[8]\nNow many people have not unnaturally thought it derogatory\nto genius to suggest that its productions could\nhave also been obtained by chance, whilst others have gone\non to argue, If this be the case, might not the world itself in\nthis manner have been produced by chance?\n\n22. We will begin with the comparatively simple, determinate,\nand intelligible problem of the possible production\nof the works of a great human genius by chance. With\nregard to this possibility, it may be a consolation to some\ntimid minds to be reminded that the power of producing the\nworks of a Shakespeare, _in time_, is not confined to consummate\ngenius and to mere chance. There is a third alternative,\nviz. that of purely mechanical procedure. Any one,\ndown almost to an idiot, might do it, if he took sufficient\ntime about the task. For suppose that the required number\nof letters were procured and arranged, not by chance, but\ndesignedly, and according to rules suggested by the theory\nof permutations: the letters of the alphabet and the number\nof them to be employed being finite, every order in which\nthey could occur would come in its due turn, and therefore\nevery thing which can be expressed in language would be\narrived at some time or other.\n\nThere is really nothing that need shock any one in such\na result. Its possibility arises from the following cause.\nThe number of letters, and therefore of words, at our disposal\nis limited; whatever therefore we may desire to express\nin language necessarily becomes subject to corresponding\nlimitation. The possible variations of thought are literally\ninfinite, so are those of spoken language (by intonation of\nthe voice, &c.); but when we come to words there is a limitation,\nthe nature of which is distinctly conceivable by the\nmind, though the restriction is one that in practice will\nnever be appreciable, owing to the fact that the number of\ncombinations which may be produced is so enormous as to\nsurpass all power of the imagination to realize.[9] The answer\ntherefore is plain, and it is one that will apply to many other\ncases as well, that to put a finite limit upon the number of\nways in which a thing can be done, is to determine that any\none who is able and willing to try long enough shall succeed\nin doing it. If a great genius condescends to perform it\nunder these circumstances, he must submit to the possibility\nof having his claims rivalled or disputed by the chance-man\nand idiot. If Shakespeare were limited to the use of eight\nor nine assigned words, the time within which the latter\nagents might claim equality with him would not be very\ngreat. As it is, having had the range of the English language\nat his disposal, his reputation is not in danger of being\nassailed by any such methods.\n\n23. The case of the possible production of the world\nby chance leads us into an altogether different region of discussion.\nWe are not here dealing with figures the nature\nand use of which are within the fair powers of the understanding,\nhowever the imagination may break down in attempting\nto realize the smallest fraction of their full significance.\nThe understanding itself is wandering out of its\nproper province, for the conditions of the problem cannot be\nassigned. When we draw letters out of a bag we know very\nwell what we are doing; but what is really meant by producing\na world by chance? By analogy of the former case,\nwe may assume that some kind of agent is presupposed;--perhaps\ntherefore the following supposition is less absurd\nthan any other. Imagine some being, not a Creator but a\nsort of Demiurgus, who has had a quantity of materials put\ninto his hands, and he assigns them their collocations and\ntheir laws of action, blindly and at haphazard: what are the\nodds that such a world as we actually experience should have\nbeen brought about in this way?\n\nIf it were worth while seriously to set about answering\nsuch a question, and if some one would furnish us with the\nnumber of the letters of such an alphabet, and the length of\nthe work to be written with them, we could proceed to indicate\nthe result. But so much as this may surely be affirmed\nabout it;--that, far from merely finding the length of this\nsmall volume insufficient for containing the figures in which\nthe adverse odds would be given, all the paper which the\nworld has hitherto produced would be used up before we had\ngot far on our way in writing them down.\n\n24. The most seductive form in which the difficulty\nabout the occurrence of very rare events generally presents\nitself is probably this. 'You admit (some persons will be\ndisposed to say) that such an event may sometimes happen;\nnay, that it does sometimes happen in the infinite course of\ntime. How then am I to know that _this_ occasion is not one\nof these possible occurrences?' To this, one answer only can\nbe given,--the same which must always be given where\nstatistics and probability are concerned,--'The present _may_\nbe such an occasion, but it is inconceivably unlikely that it\nshould be one. Amongst countless billions of times in which\nyou, and such as you, urge this, one person only will be\njustified; and it is not likely that you are that one, or that\nthis is that occasion.'\n\n25. There is another form of this practical inability to\ndistinguish between one high number and another in the\nestimation of chances, which deserves passing notice from its\nimportance in arguments about heredity. People will often\nurge an objection to the doctrine that qualities, mental and\nbodily, are transmitted from the parents to the offspring, on\nthe ground that there are a multitude of instances to the\ncontrary, in fact a great majority of such instances. To\nraise this objection implies an utter want of appreciation of\nthe very great odds which possibly may exist, and which the\nargument in support of heredity implies _do_ exist against any\ngiven person being distinguished for intellectual or other\neminence. This is doubtless partly a matter of definition,\ndepending upon the degree of rarity which we consider to be\nimplied by eminence; but taking any reasonable sense of the\nterm, we shall readily see that a very great proportion of\nfailures may still leave an enormous preponderance of evidence\nin favour of the heredity doctrine. Take, for instance,\nthat degree of eminence which is implied by being one of\nfour thousand. This is a considerable distinction, though,\nsince there are about two thousand such persons to be found\namongst the total adult male population of Great Britain, it\nis far from implying any conspicuous genius. Now suppose\nthat in examining the cases of a large number of the children\nof such persons, we had found that 199 out of 200 of\nthem failed to reach the same distinction. Many persons\nwould conclude that this was pretty conclusive evidence\nagainst any hereditary transmission. To be able to adduce\nonly one favourable, as against 199 hostile instances, would\nto them represent the entire break-down of any such theory.\nThe error, of course, is obvious enough, and one which, with\nthe figures thus before him, hardly any one could fail to\navoid. But if one may judge from common conversation\nand other such sources of information, it is found in practice\nexceedingly difficult adequately to retain the conviction that\neven though only one in 200 instances were favourable,\nthis would represent odds of about 20 to 1 in favour of the\ntheory. If hereditary transmission did not prevail, only one\nin 4000 sons would thus rival their fathers; but we find\nactually, let us say (we are of course taking imaginary proportions\nhere), that one in 200 does. Hence, if the statistics\nare large enough to be satisfactory, there has been some\ninfluence at work which has improved the chances of mere\ncoincidence in the ratio of 20 to 1. We are in fact so little\nable to realise the meaning of very large numbers,--that is,\nto retain the _ratios_ in the mind, where large numbers are\nconcerned,--that unless we repeatedly check ourselves by\narithmetical considerations we are too apt to treat and estimate\nall beyond certain limits as equally vast and vague.\n\n26. (VI.) In discussing the nature of the connexion\nbetween Probability and Induction, we examined the claims\nof a rule commonly given for inferring the probability that\nan event which had been repeatedly observed would recur\nagain. I endeavoured to show that all attempts to obtain\nand prove such a rule were necessarily futile; if these reasons\nwere conclusive the employment of such a rule must of\ncourse be regarded as fallacious. A few examples may conveniently\nbe added here, tending to show how instead of\nthere being merely a single rule of succession we might better\ndivide the possible forms into three classes.\n\n(1) In some cases when a thing has been observed to\nhappen several times it becomes in consequence _more_ likely\nthat the thing should happen again. This agrees with the\nordinary form of the rule, and is probably the case of most\nfrequent occurrence. The necessary vagueness of expression\nwhen we talk of the 'happening of a thing' makes it quite\nimpossible to tolerate the rule in this general form, but if we\nspecialize it a little we shall find it assume a more familiar\nshape. If, for example, we have observed two or more properties\nto be frequently associated together in a succession of\nindividuals, we shall conclude with some force that they will\nbe found to be so connected in future. The strength of our\nconviction however will depend not merely on the number\nof observed coincidences, but on far more complicated considerations;\nfor a discussion of which the reader must be\nreferred to regular treatises on Inductive evidence. Or again,\nif we have observed one of two events succeed the other\nseveral times, the occurrence of the former will excite in\nmost cases some degree of expectation of the latter. As\nbefore, however, the degree of our expectation is not to be\nassigned by any simple formula; it will depend in part upon\nthe supposed intimacy with which the events are connected.\nTo attempt to lay down definite rules upon the subject\nwould lead to a discussion upon laws of causation, and the\ncircumstances under which their existence may be inferred,\nand therefore any further consideration of the matter must\nbe abandoned here.\n\n27. (2) Or, secondly, the past recurrence may in itself\ngive no valid grounds for inference about the future;\nthis is the case which most properly belongs to Probability.[10]\nThat it does so belong will be easily seen if we bear in mind\nthe fundamental conception of the science. We are there\nintroduced to a series,--for purposes of inference an indefinitely\nextended series,--of terms, about the details of which,\ninformation, except on certain points, is not given; our knowledge\nbeing confined to the statistical fact, that, say, one in\nten of them has some attribute which we will call X. Suppose\nnow that five of these terms in succession have been X,\nwhat hint does this give about the sixth being also an X?\nClearly none at all; this past fact tells us nothing; the formula\nfor our inference is still precisely what it was before,\nthat one in ten being X it is one to nine that the next term\nis X. And however many terms in succession had been of\none kind, precisely the same formula would still be given.\n\n28. The way in which events will justify the answer\ngiven by this formula is often misunderstood. For the\nbenefit therefore of those unacquainted with some of the\nconceptions familiar to mathematicians, a few words of explanation\nmay be added. Suppose then that we have had\nX twelve times in succession. This is clearly an anomalous\nstate of things. To suppose anything like this continuing\nto occur would be obviously in opposition to the statistics,\nwhich assert that in the long run only one in ten is X.\nBut how is this anomaly got over? In other words, how\ndo we obviate the conclusion that X's must occur more\nfrequently than once in ten times, after such a long succession\nof them as we have now had? Many people seem to\nbelieve that there must be a diminution of X's afterwards\nto counterbalance their past preponderance. This however\nwould be quite a mistake; the proportion in which they\noccur in future must remain the same throughout; it cannot\nbe altered if we are to adhere to our statistical formula.\nThe fact is that the rectification of the exceptional disturbance\nin the proportion will be brought about simply by the\ncontinual influx of fresh terms in the series. These will in\nthe long run neutralize the disturbance, not by any special\nadaptation, as it were, for the purpose, but by the mere\nweight of their overwhelming numbers. At every stage\ntherefore, in the succession, whatever might have been the\nnumber and nature of the preceding terms, it will still be\ntrue to say that one in ten of the terms will be an X.\n\nIf we had to do only with a finite number of terms,\nhowever large that number might be, such a disturbance as\nwe have spoken of would, it is true, need a special alteration\nin the subsequent proportions to neutralize its effects. But\nwhen we have to do with an infinite number of terms, this\nis not the case; the 'limit' of the series, which is what we\nthen have to deal with, is unaffected by these temporary\ndisturbances. In the continued progress of the series we\nshall find, as a matter of fact, more and more of such disturbances,\nand these of a more and more exceptional character.\nBut whatever the point we may occupy at any time, if we\nlook forward or backward into the indefinite extension of the\nseries, we shall still see that the ultimate limit to the proportion\nin which its terms are arranged remains the same;\nand it is with this limit, as above mentioned, that we are\nconcerned in the strict rules of Probability.\n\nThe most familiar example, perhaps, of this kind is that\nof tossing up a penny. Suppose we have had four heads in\nsuccession; people[11] have tolerably realized by now that 'head\nthe fifth time' is still an even chance, as 'head' was each\ntime before, and will be ever after. The preceding paragraph\nexplains how it is that these occasional disturbances\nin the average become neutralized in the long run.\n\n29. (3) There are other cases which, though rare,\nare by no means unknown, in which such an inference as\nthat obtained from the Rule of Succession would be the direct\nreverse of the truth. The oftener a thing happens, it\nmay be, the more unlikely it is to happen again. This is the\ncase whenever we are drawing things from a limited source\n(as balls from a bag without replacing them), or whenever\nthe act of repetition itself tends to prevent the succession\n(as in giving false alarms).\n\nI am quite ready to admit that we believe the results described\nin the last two classes on the strength of some such\ngeneral Inductive rule, or rather principle, as that involved\nin the first. But it would be a great error to confound this\nwith an admission of the validity of the rule in each special\ninstance. We are speaking about the application of the rule\nto individual cases, or classes of cases; this is quite a distinct\nthing, as was pointed out in a previous chapter, from\ngiving the grounds on which we rest the rule itself. If a\nman were to lay it down as a universal rule, that the testimony\nof all persons was to be believed, and we adduced an\ninstance of a man having lied, it would not be considered\nthat he saved his rule by showing that we believed that it\nwas a lie on the word of other persons. But it is perfectly\nconsistent to give as a merely general, but not universal,\nrule, that the testimony of men is credible; then to separate\noff a second class of men whose word is not to be trusted,\nand finally, if any one wants to know our ground for the\nsecond rule, to rest it upon the first. If we were speaking\nof _necessary_ laws, such a conflict as this would be as\nhopeless as the old 'Cretan' puzzle in logic; but in instances\nof Inductive and Analogical extension it is perfectly\nharmless.\n\n30. A familiar example will serve to bring out the\nthree different possible conclusions mentioned above. We\nhave observed it rain on ten successive days. A and B conclude\nrespectively for and against rain on the eleventh day;\nC maintains that the past rain affords no data whatever for\nan opinion. Which is right? We really cannot determine\n_\u00e0 priori_. An appeal must be made to direct observation, or\nmeans must be found for deciding on independent grounds\nto which class we are to refer the instance. If, for example,\nit were known that every country produces its own rain, we\nshould choose the third rule, for it would be a case of drawing\nfrom a limited supply. If again we had reasons to believe\nthat the rain for our country might be produced anywhere\non the globe, we should probably conclude that the past\nrainfall threw no light whatever on the prospect of a continuance\nof wet weather, and therefore take the second.\nOr if, finally, we knew that rain came in long spells or seasons,\nas in the tropics, then the occurrence of ten wet days\nin succession would make us believe that we had entered on\none of these seasons, and that therefore the next day would\nprobably resemble the preceding ten.\n\nSince then all these forms of such an Inductive rule are\npossible, and we have often no _\u00e0 priori_ grounds for preferring\none to another, it would seem to be unreasonable to attempt\nto establish any universal formula of anticipation. All that\nwe can do is to ascertain what are the circumstances under\nwhich one or other of these rules is, as a matter of fact,\nfound to be applicable, and to make use of it under those\ncircumstances.\n\n31. (VII.) In the cases discussed in (V.) the almost\ninfinitely small chances with which we were concerned were\nrightly neglected from all practical consideration, however\nproper it might be, on speculative grounds, to keep our minds\nopen to their actual existence. But it has often occurred to\nme that there is a common error in neglecting to take them into\naccount when they may, though individually small, make up\nfor their minuteness by their number. As the mathematician\nwould express it, they may occasionally be capable of being\n_integrated_ into a finite or even considerable magnitude.\n\nFor instance, we may be confronted with a difficulty out\nof which there appears to be only one appreciably possible\nmode of escape. The attempt is made to force us into\naccepting this, however great the odds apparently are against\nit, on the ground that improbable as it may seem, it is at\nany rate vastly more probable than any of the others. I\ncan quite admit that, on practical grounds, we may often find\nit reasonable to adopt this course; for we can only _act_ on\none supposition, and we naturally and rightly choose, out\nof a quantity of improbabilities, the least improbable. But\nwhen we are not forced to act, no such decisive preference is\ndemanded of us. It is then perfectly reasonable to refuse\nassent to the proposed explanation; even to say distinctly\nthat we do not believe it, and at the same time to decline,\nat present, to accept any other explanation. We remain, in\nfact, in a state of suspense of judgment, a state perfectly\nright and reasonable so long as no action demanding a specific\nchoice is forced upon us. One alternative may be\ndecidedly probable as compared with any other individually,\nbut decidedly improbable as compared with all others collectively.\nThis in itself is intelligible enough; what people\noften fail to see is that there is no necessary contradiction\nbetween saying and feeling this, and yet being prepared\nvigorously to act, when action is forced upon us, as though\nthis alternative were really the true one.\n\n32. To take a specific instance, this way of regarding\nthe matter has often occurred to me in disputes upon 'Spiritualist'\nmanifestations. Assent is urged upon us because,\nit is said, no other possible solution can be suggested. It\nmay be quite true that apparently overwhelming difficulties\nmay lie as against each separate alternative solution; but is\nit always sufficiently realized how numerous such solutions\nmay be? No matter that each individually may be almost\nincredible: they ought all to be massed together and thrown\ninto the scale against the proffered solution, when the only\nquestion asked is, Are we to accept this solution? There is\nno unfairness in such a course. We are perfectly ready to\nadopt the same plan against any other individual alternative,\nwhenever any person takes to claiming this as _the_\nsolution of the difficulty. We are looking at the matter\nfrom a purely logical point of view, and are quite willing, so\nfar, to place every solution, spiritualist or otherwise, upon the\nsame footing. The partisans of every alternative are in\nsomewhat the same position as the members of a deliberative\nassembly, in which no one will support the motion of any\nother member. Every one can aid effectively in rejecting\nevery other motion, but no one can succeed in passing his\nown. Pressure of urgent necessity may possibly force them\nout of this state of practical inaction, by, so to say, breaking\nthrough the opposition at some point of least resistance; but\nunless aided by some such pressure they are left in a state of\nhopeless dead-lock.\n\n33. Assuming that the spiritualistic solution admits\nof, and is to receive, scientific treatment, this, it seems to\nme, is the conclusion to which one might sometimes be led\nin the face of the evidence offered. We might have to say to\nevery individual explanation, It is incredible, I cannot accept\nit; and unless circumstances should (which it is hardly possible\nthat they should) force us to a hasty decision,--a decision,\nremember, which need indicate no preference of the\njudgment beyond what is just sufficient to turn the scale in its\nfavour as against any other single alternative,--we leave the\nmatter thus in abeyance. It will very likely be urged that\none of the explanations (assuming that all the possible ones\nhad been included) must be true; this we readily admit.\nIt will probably also be urged that (on the often-quoted\nprinciple of Butler) we ought forthwith to accept the one\nwhich, as compared with the others, is the most plausible,\nwhatever its absolute worth may be. This seems distinctly\nan error. To say that such and such an explanation is the\none we should accept, _if_ circumstances compelled us to anticipate\nour decision, is quite compatible with its present\nrejection. The only rational position surely is that of\nadmitting that the truth is somewhere amongst the various\nalternatives, but confessing plainly that we have no such\npreference for one over another as to permit our saying anything\nelse than that we disbelieve each one of them.\n\n34. (VIII.) The very common fallacy of 'judging by\nthe event,' as it is generally termed, deserves passing notice\nhere, as it clearly belongs to Probability rather than to Logic;\nthough its nature is so obvious to those who have grasped the\ngeneral principles of our science, that a very few words of\nremark will suffice. In one sense every proposition must\nconsent to be judged by the event, since this is merely, in\nother words, submitting it to the test of experience. But\nthere is the widest difference between the test appropriate\nto a universal proposition and that appropriate to a merely\nproportional or statistical one. The former is subverted by a\nsingle exception; the latter not merely admits exceptions,\nbut implies them. Nothing, however, is more common than\nto blame advice (in others) because it has happened to turn\nout unfortunately, or to claim credit for it (in oneself) because\nit has happened to succeed. Of course if the conclusion was\navowedly one of a probable kind we must be prepared with\ncomplacency to accept a hostile event, or even a succession of\nthem; it is not until the succession shows a disposition to\ncontinue over long that suspicion and doubt should arise, and\nthen only by a comparison of the degree of the assigned\nprobability, and the magnitude of the departure from it\nwhich experience exhibits. For any single failure the reply\nmust be, 'the advice was sound' (supposing, that is, that it\nwas to be justified in the long run), 'and I shall offer it again\nunder the same circumstances.'\n\n35. The distinction drawn in the above instance\ndeserves careful consideration; for owing to the wide difference\nbetween the kind of propositions dealt with in Probability\nand in ordinary Logic, and the consequent difference in\nthe nature of the proof offered, it is quite possible for arguments\nof the same general appearance to be valid in the\nformer and fallacious in the latter, and conversely.\n\nFor instance, take the well-known fallacy which consists\nin simply converting a universal affirmative, i.e. in passing\nfrom All A is B to All B is A. When, as in common Logic,\nthe conclusion is to be as certain as the premise, there is not\na word to be said for such a step. But if we look at the\nprocess with the more indulgent eye of Induction or Probability\nwe see that a very fair case may sometimes be made\nout for it. The mere fact that 'Some B is A' raises a certain\npresumption that any particular B taken at random will\nbe an A. There is some reason, at any rate, for the belief,\nthough in the absence of statistics as to the relative frequency\nof A and B we are unable to assign a value to this\nbelief. I suspect that there may be many cases in which a\nman has inferred that some particular B is an A on the\nground that All A is B, who might justly plead in his behalf\nthat he never meant it to be a necessary, but only a probable\ninference. The same remarks will of course apply\nalso to the logical fallacy of Undistributed Middle.\n\nNow for a case of the opposite kind, i.e. one in which\nProbability fails us, whereas the circumstances seem closely\nanalogous to those in which ordinary inference would be\nable to make a stand. Suppose that I know that one letter\nin a million is lost when in charge of the post. I write to a\nfriend and get no answer. Have I any reason to suppose\nthat the fault lies with him? Here is an event (viz. the\nloss of the letter) which has certainly happened; and we suppose\nthat, of the only two causes to which it can be assigned,\nthe 'value,' i.e. statistical frequency, of one is accurately\nassigned, does it not seem natural to suppose that something\ncan be inferred as to the likelihood that the other cause had\nbeen operative? To say that nothing can be known about\nits adequacy under these circumstances looks at first sight\nlike asserting that an equation in which there is only one\nunknown term is theoretically insoluble.\n\nAs examples of this kind have been amply discussed in\nthe chapter upon Inverse rules of Probability I need do no\nmore here than remind the reader that no conclusion whatever\ncan be drawn as to the likelihood that the fault lay\nwith my friend rather than with the Post Office. Unless we\neither know, or make some assumption about, the frequency\nwith which he neglects to answer the letters he receives, the\nproblem remains insoluble.\n\nThe reason why the apparent analogy, indicated above,\nto an equation with only one unknown quantity, fails to hold\ngood, is that for the purposes of Probability there are really\n_two_ unknown quantities. What we deal with are proportional\nor statistical propositions. Now we are only told that\nin the instance in question the letter was lost, not that they\nwere found to be lost in such and such a proportion of cases.\nHad this latter information been given to us we should really\nhave had but one unknown quantity to determine, viz. the\nrelative frequency with which my correspondent neglects to\nanswer his letters, and we could then have determined this\nwith the greatest ease.\n\n\n1. Discussed by Mr F. Y. Edgeworth, in the _Phil. Mag._ for April,\n  1887.\n\n2. _Journal of the Statistical Soc._ (Vol. XLII. p. 328) Dare one\n  suspect a joke?\n\n3. It appears to have been long known to gamblers under the name of\n  the _Martingale_. There is a paper by Babbage (_Trans. of Royal\n  Soc. of Edinburgh_, for 1823) which discusses certain points\n  connected with it, but scarcely touches on the subject of the\n  sections which follow.\n\n4. Attention will be further directed to this distinction in the\n  chapter on Insurance and Gambling.\n\n5. As by Pr\u00e9vost in the _Biblioth\u00e8que Universelle de Gen\u00e8ve_,\n  Oct. 1829. The explanation is noted, and apparently accepted, by\n  Quetelet (_Physique Sociale_, I. 171).\n\n6. _Essay on Probabilities_, p. 126.\n\n7. This theoretical or absolute neglect of what is very rare must not\n  be confused with the practical neglect sometimes recommended by\n  astronomical and other observers. A criterion, known as Chauvenet's,\n  for indicating the limits of such rejection will be found described\n  in Mr Merriman's _Least Squares_ (p. 166). But this rests on the\n  understanding that a smaller balance of error would thus result in\n  the long run. The very rare event is deliberately rejected, not\n  overlooked.\n\n8. The process of calculation may be readily indicated. There are,\n  say, about 350,000 letters in the work in question. Since any of the\n  26 letters of the alphabet may be drawn each time, the possible\n  number of combinations would be 26^{350,000}; a number which, as may\n  easily be inferred from a table of logarithms, would demand for its\n  expression nearly 500,000 figures. Only one of these combinations is\n  favourable, if we reject variations of spelling. Hence unity divided\n  by this number would represent the chance of getting the desired\n  result by successive random selection of the required number of\n  350,000 letters.\n\n  If this chance is thought too small, and any one asks how often the\n  above random selection must be repeated in order to give him odds of\n  2 to 1 in favour of success, this also can be easily shown. If the\n  chance of an event on each occasion is 1/n, the chance of getting it\n  once at least in n trials is 1 - ((n - 1)/n)^{n}; for we shall do\n  this unless we fail n times running. When (as in the case in\n  question) n is very large, this may be shown algebraically to be\n  equivalent to odds of about 2 to 1. That is, when we have drawn the\n  requisite quantity of letters a number of times equal to the\n  inconceivably great number above represented, it is still only 2 to\n  1 that we shall have secured what we want:--and then we have to\n  recognize it.\n\n9. The longest life which could reasonably be attributed to any\n  language would of course dwindle into utter insignificance in the\n  face of such periods of time as are being here arithmetically\n  contemplated.\n\n10. We are here assuming of course that the ultimate limit to which\n  our average tends is known, either from knowledge of the causes or\n  from previous extensive experience. We are assuming that e.g. the\n  die is known to be a fair one; if this is not known but a possible\n  bias has to be inferred from its observed performances, the case\n  falls under the former head.\n\n11. Except indeed the gamblers. According to a gambling acquaintance\n  whom Houdin, the conjurer, describes himself as having met at Spa,\n  \"the oftener a particular combination has occurred the more certain\n  it is that it will not be repeated at the next _coup_: this is the\n  groundwork of all theories of probabilities and is termed the\n  maturity of chances\" (_Card-sharping exposed_, p. 85).\n\n\n\n\nCHAPTER XV.\n\n\n_INSURANCE AND GAMBLING._\n\n1. If the reader will recall to mind the fundamental\npostulate of the Science of Probability, established and explained\nin the first few chapters, and so abundantly illustrated\nsince, he will readily recognize that the two opposite\ncharacteristics of individual irregularity and average regularity\nwill naturally be differently estimated by different\nminds. To some persons the elements of uncertainty may\nbe so painful, either in themselves or in their consequences,\nthat they are anxious to adopt some means of diminishing\nthem. To others the ultimate regularity of life, at any rate\nwithin certain departments, its monotony as they consider it,\nmay be so wearisome that _they_ equally wish to effect some\nalteration and improvement in its characteristics. We shall\ndiscuss briefly these mental tendencies, and the most simple\nand obvious modes of satisfying them.\n\nTo some persons, as we have said, the world is all too full\nof change and irregularity and consequent uncertainty. Civilization\nhas done much to diminish these characteristics in\ncertain directions, but it has unquestionably aggravated them\nin other directions, and it might not be very easy to say with\ncertainty in which of these respects its operation has been, at\npresent, on the whole most effective. The diminution of\nirregularity is exemplified, amongst other things, in the case\nof the staple products which supply our necessary food and\nclothing. With respect to them, famine and scarcity are by\ncomparison almost unknown now, at any rate in tolerably\ncivilized communities. As a consequence of this, and of the\nvast improvements in the means of transporting goods and\nconveying intelligence, the fluctuations in the price of such\narticles are much less than they once were. In other directions,\nhowever, the reverse has been the case. Fashion, for\ninstance, now induces so many people in every large community\nsimultaneously to desire the same thing, that great\nfluctuations in value may ensue. Moreover a whole group of\ncauses (to enter upon any discussion of which would be to\ntrench upon the ground of Political Economy) combine to\nproduce great and frequent variations in matters concerning\ncredit and the currency, which formerly had no existence.\nBankruptcy, for instance, is from the nature of the case,\nalmost wholly a creation of modern times. We will not attempt\nto strike any balance between these opposite results\nof modern civilization, beyond remarking that in matters of\nprime importance the actual uncertainties have been probably\non the whole diminished, whereas in those which affect\nthe pocket rather than the life, they have been rather increased.\nIt might also be argued with some plausibility\nthat in cases where the actual uncertainties have not become\ngreater, they have for all practical purposes done so, by their\nconsequences frequently becoming more serious, or by our\nestimate of these consequences becoming higher.\n\n2. However the above question, as to the ultimate\nbalance of gain or loss, should be decided, there can be no\ndoubt that many persons find the present amount of uncertainty\nin some of the affairs of life greater than suits their\ntaste. How are they to diminish it? Something of course\nmay be done, as regards the individual cases, by prudence\nand foresight. Our houses may be built with a view not to\ntake fire so readily, or precautions may be taken that there\nshall be fire-engines at hand. In the warding off of death\nfrom disease and accident, something may be done by every\none who chooses to live prudently. Precautions of the above\nkind, however, do not introduce any questions of Probability.\nThese latter considerations only come in when we begin to\ninvoke the regularity of the average to save us from the\nirregularities of the details. We cannot, it is true, remove\nthe uncertainty in itself, but we can so act that the consequences\nof that uncertainty shall be less to us, or to those in\nwhom we are interested. Take the case of Life Insurance.\nA professional man who has nothing but the income he earns\nto depend upon, knows that the whole of that income may\nvanish in a moment by his death. This is a state of things\nwhich he cannot prevent; and if he were the only one in\nsuch a position, or were unable or unwilling to combine with\nhis fellow-men, there would be nothing more to be done in\nthe matter except to live within his income as much as possible,\nand so leave a margin of savings.\n\n3. There is however an easy mode of escape for him.\nAll that he has to do is to agree with a number of others,\nwho are in the same position as himself, to make up, so to\nsay, a common purse. They may resolve that those of their\nnumber who live to work beyond the average length of life\nshall contribute to support the families of those who die\nearlier. If a few only concurred in such a resolution they\nwould not gain very much, for they would still be removed\nby but a slight step from that uncertainty which they are\nseeking to escape. What is essential is that a considerable\nnumber should thus combine so as to get the benefit of that\ncomparative regularity which the average, as is well known,\nalmost always tends to exhibit.\n\n4. The above simple considerations really contain the\nessence of all insurance. Such points as the fact that the\nagreement for indemnity extends only to a certain definite\nsum of money; and that instead of calling for an occasional\ngeneral contribution at the time of the death of each member\nthey substitute a fixed annual premium, out of the proceeds\nof which the payment is to be made, are merely accidents of\nconvenience and arrangement. Insurance is simply equivalent\nto a mutual contract amongst those who dread the consequences\nof the uncertainty of their life or employment,\nthat they will employ the aggregate regularity to neutralize\nas far as possible the individual irregularity. They know\nthat for every one who gains by such a contract another will\nlose as much; or if one gains a great deal many must have\nlost a little. They know also that hardly any of their number\ncan expect to find the arrangement a 'fair' one, in the\nsense that they just get back again what they have paid in\npremiums, after deducting the necessary expenses of management;\nbut they deliberately prefer this state of things.\nThey consist of a body of persons who think it decidedly\nbetter to leave behind them a comparatively fixed fortune,\nrather than one which is extremely uncertain in amount;\nalthough they are perfectly aware that, owing to the unavoidable\nexpenses of managing the affairs of such a society,\nthe comparatively fixed sum, so to be left, will be a trifle less\nthan the average fortunes which would have been left had\nno such system of insurance been adopted.\n\nAs this is not a regular treatise upon Insurance no more\nneed be said upon the exact nature of such societies, beyond\npointing out that they are of various different kinds. Sometimes\nthey really are what we have compared them with,\nviz. mutual agreements amongst a group of persons to make\nup each other's losses to a certain extent. Into this category\nfall the Mutual Insurance Societies, Benefit Societies, Trades\nUnions (in respect of some of their functions), together with\ninnumerable other societies which go by various names.\nSometimes they are companies worked by proprietors or\nshareholders for a profit, like any other industrial enterprise.\nThis is the case, I believe, with the majority of the\nordinary Life Insurance Societies. Sometimes, again, it is\nthe State which undertakes the management, as in the case\nof our Post Office Insurance business.\n\n5. It is clear that there is no necessary limit to the\nrange of application of this principle.[1] It is quite conceivable\nthat the majority of the inhabitants of some nation\nmight be so enamoured of security that they should devise\na grand insurance society to cover almost every concern in\nlife. They could not indeed abolish uncertainty, for the\nconditions of life are very far from permitting this, but they\ncould without much difficulty get rid of the worst of the\n_consequences_ of it. They might determine to insure not\nmerely their lives, houses, ships, and other things in respect\nof which sudden and total loss is possible, but also\nto insure their business; in the sense of avoiding not only\nbankruptcy, but even casual bad years, on the same principle\nof commutation. Unfamiliar as such an aim may appear\nwhen introduced in this language, it is nevertheless one\nwhich under a name of suspicious import to the conservative\nclasses has had a good deal of attention directed to it. It is\nreally scarcely anything else than Communism, which might\nindeed be defined as a universal and compulsory[2] insurance\nsociety which is to take account of all departments of business,\nand, in some at least of its forms, to invade the province\nof social and domestic life as well.\n\nAlthough nothing so comprehensive as this is likely to\nbe practically carried out on any very large scale, it deserves\nnotice that the principle itself is steadily spreading in every\ndirection in matters of detail. It is, for instance, the great\ncomplaint against Trades Unions that they too often seek to\nsecure these results in respect of the equalization of the\nworkmen's wages, thus insuring to some degree against incompetence,\nas they rightly and wisely do against illness and\nloss of work. Again, there is the Tradesman's Mutual Protection\nSociety, which insures against the occasional loss\nentailed by the necessity of having to conduct prosecutions\nat law. There are societies in many towns for the prosecution\nof petty thefts, with the object of escaping the same\nuncertain and perhaps serious loss. Amongst instances of\ninsurance _for_ the people rather than _by_ them, there is of\ncourse the giant example of the English Poor Law, in\nwhich the resemblance to an initial Communistic system\nbecomes very marked. The poor are insured against loss\nof work arising not only from illness and old age, but from\nany cause except wilful idleness. They do not, it is true,\npay the whole premium, but since they mostly bear some\nportion of the burden of municipal and county taxation\nthey must certainly be considered as paying a part of\nthe premium. In some branches also of the public and\nprivate services the system is adopted of deducting a percentage\nfrom the wage or salary, for the purpose of a\nsemi-compulsory insurance against death, illness or superannuation.\n\n6. Closely connected with Insurance, as an application\nof Probability, though of course by contrast, stands Gambling.\nThough we cannot, in strictness, term either of these practices\nthe converse of the other, it seems nevertheless correct\nto say that they spring from opposite mental tendencies.\nSome persons, as has been said, find life too monotonous for\ntheir taste, or rather the region of what can be predicted\nwith certainty is too large and predominant in their estimation.\nThey can easily adopt two courses for securing the\nchanges they desire. They may, for one thing, aggravate\nand intensify the results of events which are comparatively\nincapable of prevision, these events not being in themselves\nof sufficient importance to excite any strong emotions. The\nmost obvious way of doing this is by betting upon them.\nOr again, they may invent games or other pursuits, the\nindividual contingencies of which are entirely removed from\nall possible human prevision, and then make heavy money\nconsequences depend upon these contingencies. This is\ngambling proper, carried on mostly by means of cards and\ndice and the roulette.\n\nThe gambling spirit, as we have said, seeks for the excitement\nof uncertainty and variety. When therefore people\nmake a long continued practice of playing, especially if the\nstakes for which they play are moderate in comparison with\ntheir fortune, this uncertainty from the nature of the case\nbegins to diminish. The thoroughly practised gambler, if\nhe possesses more than usual skill (in games where skill\ncounts for something), must be regarded as a man following\na profession, though a profession for the most part of a risky\nand exciting kind, to say nothing of its ignoble and often\ndishonest character. If, on the other hand, his skill is below\nthe average, or the game is one in which skill does not tell\nand the odds are slightly in favour of his antagonist, as in\nthe gaming tables, one light in which he can be regarded\nis that of a man who is following a favourite amusement;\nif this amusement involves a constant annual outlay on his\npart, that is nothing more than what has to be said of most\nother amusements.\n\n7. We cannot, of course, give such a rational explanation\nas the above in every case. There are plenty of\nnovices, and plenty of fanatics, who go on steadily losing in\nthe full conviction that they will eventually come out winners.\nBut it is hard to believe that such ignorance, or such\nintellectual twist, can really be so widely prevalent as would\nbe requisite to constitute them the rule rather than the exception.\nThere must surely be some very general impulse\nwhich is gratified by such resources, and it is not easy to see\nwhat else this can be than a love of that variety and consequent\nexcitement which can only be found in perfection\nwhere exact prevision is impossible.\n\nIt is of course very difficult to make any generalization\nhere as to the comparative prevalence of various motives\namongst mankind; but when one considers what is the\ndifference which most quiet ordinary whist players feel\nbetween a game for 'love' and one in which there is a\nsmall stake, one cannot but assign a high value to the\ninfluence of a wish to emphasize the excitement of loss\nand gain.\n\nI would not for a moment underrate the practical dangers\nwhich are found to attend the practice of gambling. It\nis remarked that the gambler, if he continues to play for a\nlong time, is under an almost irresistible impulse to increase\nhis stakes, and so re-introduce the element of uncertainty.\nIt is in fact this tendency to be thus led on, which makes\nthe principal danger and mischief of the practice. Risk and\nuncertainty are still such normal characteristics of even civilized\nlife, that the mere extension of such tendencies into\nnew fields does not in itself offer any very alarming prospect.\nIt is only to be deprecated in so far as there is a\ndanger, which experience shows to be no trifling one, that\nthe fascination found in the pursuit should lead men into\nfollowing it up into excessive lengths.[3]\n\n8. The above general treatment of Gambling and\nInsurance seems to me the only rational and sound principle\nof division;--namely, that on which the different practices\nwhich, under various names, are known as gambling\nor insurance, are arranged in accordance with the spirit of\nwhich they are the outcome, and therefore of the results\nwhich they are designed to secure. If we were to attempt\nto judge and arrange them according to the names which\nthey currently bear, we should find ourselves led to no\nkind of systematic division whatever; the fact being that\nsince they all alike involve, as their essential characteristic,\npayments and receipts, one or both of which are necessarily\nuncertain in their date or amount, the names may often be\ninterchanged.\n\nFor instance, a lottery and an ordinary insurance society\nagainst accident, if we merely look to the processes performed\nin them, are to all intents and purposes identical.\nIn each alike there is a small payment which is certain in\namount, and a great receipt which is uncertain in amount.\nA great many persons pay the small premium, whereas a\nfew only of their number obtain a prize, the rest getting\nno return whatever for their outlay. In each case alike,\nalso, the aggregate receipts and losses are intended to\nbalance each other, after allowing for the profits of those\nwho carry on the undertaking. But of course when we\ntake into account the occasions upon which the insurers\nget their prizes, we see that there is all the difference in the\nworld between receiving them at haphazard, as in a lottery,\nand receiving them as a partial set-off to a broken limb or\ninjured constitution, as in the insurance society.\n\nAgain, the language of betting may be easily made to\ncover almost every kind of insurance. Indeed De Morgan\nhas described life insurance as a bet which the individual\nmakes with the company, that he will not live beyond a\ncertain age. If he dies young, he is pecuniarily a gainer, if\nhe dies late he is a loser.[4] Here, too, though the expression\nis technically quite correct (since any such deliberate risk of\nmoney, upon an unproductive venture, may fall under the\ndefinition of a bet), there is the broadest distinction between\nbetting with no other view whatever than that of risking\nmoney, and betting with the view of diminishing risk and\nloss as much as possible. In fact, if the language of sporting\nlife is to be introduced into the matter, we ought, I presume,\nto speak of the insurer as 'hedging' against his death.\n\n9. Again, in Tontines we have a system of what is\noften called Insurance, and in certain points rightly so,\nbut which is to all intents and purposes simply and absolutely\na gambling transaction. They have been entirely\nabandoned, I believe, for some time, but were once rather\npopular, especially in France. On this plan the State, or\nwhatever society manages the business, does not gain anything\nuntil the last member of the Tontine is dead. As the\nnumber of the survivors diminishes, the same sum-total of\nannuities still continues to be paid amongst them, as long as\nany are left alive, so that each receives a gradually increasing\nsum. Hence those who die early, instead of receiving the\nmost, as on the ordinary plan, receive the least; for at the\ndeath of each member the annuity ceases absolutely, so far\nas he and his relations are concerned. The whole affair\ntherefore is to all intents and purposes a gigantic system\nof betting, to see which can live the longest; the State\nbeing the common stake-holder, and receiving a heavy commission\nfor its superintendence, this commission being naturally\nits sole motive for encouraging such a transaction. It is\nrecorded of one of the French Tontines[5] that a widow of 97\nwas left, as the last survivor, to receive an annuity of 73,500\nlivres during the rest of the life which she could manage to\ndrag on after that age;--she having originally subscribed a\nsingle sum of 300 livres only. It is obvious that such a system\nas this, though it may sometimes go by the name of insurance,\nis utterly opposed to the spirit of true insurance,\nsince it tends to aggravate existing inequalities of fortune\ninstead of to mitigate them. The insurer here bets that\nhe will die old; in ordinary insurance he bets that he will\ndie young.\n\nAgain, to take one final instance, common opinion often\nregards the bank or company which keeps a _rouge et noir_\ntable, and the individuals who risk their money at it, as being\nboth alike engaged in gambling. So they may be, technically,\nbut for all practical purposes such a bank is as sure\nand safe a business as that of any ordinary insurance society,\nand probably far steadier in its receipts than the majority of\nordinary trades in a manufacturing or commercial city. The\nbank goes in for many and small transactions, in proportion\nto its capital; their customers, very often, in proportion to\ntheir incomes go in for very heavy transactions. That the\nformer comes out a gainer year after year depends, of course,\nupon the fact that the tables are notoriously slightly in their\nfavour. But the _steadiness_ of these gains when compared\nwith the unsteadiness of the individual losses depends simply\nupon,--in fact, is merely an illustration of,--the one great\npermanent contrast which lies at the basis of all reasoning\nin Probability.\n\n10. We have so far regarded Insurance and Gambling\nas being each the product of a natural impulse, and as having\neach, if we look merely to experience, a great mass of human\njudgment in its favour. The popular moral judgment, however,\nwhich applauds the one and condemns the other rests in great\npart upon an assumption, which has doubtless much truth\nin it, but which is often interpreted with an absoluteness which\nleads to error in each direction;--the duty of insurance being\ntoo peremptorily urged upon every one, and the practice of\ngambling too universally regarded as involving a sacrifice of\nreal self-interest, as being in fact little better than a persistent\nblunder. The assumption in question seems to be\nextracted from the acknowledged advantages of insurance,\nand then invoked to condemn the practice of gambling. But\nin so doing the fact does not seem to be sufficiently recognized\nthat the latter practice, if we merely look to the extent\nand antiquity of the tacit vote of mankind in its favour,\nmight surely claim to carry the day.\n\nIt is of course obvious that in all cases with which we\nare concerned, the aggregate wealth is unaltered; money\nbeing merely transferred from one person to another. The\nloss of one is precisely equivalent to the gain of another.\nAt least this is the approximation to the truth with which we\nfind it convenient to start.[6] Now if the happiness which is\nyielded by wealth were always in direct proportion to its\namount, it is not easy to see why insurance should be advocated\nor gambling condemned. In the case of the latter this\nis obvious enough. I have lost \u00a350, say, but others (one or\nmore as the case may be) have gained it, and the increase\nof their happiness would exactly balance the diminution of\nmine. In the case of Insurance there is a slight complication,\narising from the fact that the falling in of the policy\ndoes not happen at random (otherwise, as already pointed\nout, it would be simply a lottery), but is made contingent\nupon some kind of loss, which it is intended as far as possible\nto balance. I insure myself on a railway journey, break my\nleg in an accident, and, having paid threepence for my\nticket, receive say \u00a3200 compensation from the insurance\ncompany. The same remarks, however, apply here; the\nhappiness I acquire by this \u00a3200 would only just balance the\naggregate loss of the 16,000 who have paid their threepences\nand received no return for them, were happiness always\ndirectly proportional to wealth.\n\n11. The practice of Insurance does not, I think, give\nrise to many questions of theoretic interest, and need not\ntherefore detain us longer. The fact is that it has hardly\nyet been applied sufficiently long and widely, or to matters\nwhich admit of sufficiently accurate statistical treatment,\nexcept in one department. This, of course, is Life Insurance;\nbut the subject is one which requires constant attention to\ndetails of statistics, and is (rightly) mainly carried out in\nstrict accordance with routine. As an illustration of this\nwe need merely refer to the works of De Morgan,--a professional\nactuary as well as a writer on the theory of Probability,--who\nhas found but little opportunity to aid his speculative\ntreatment of Probability by examples drawn from this class\nof considerations.\n\nWith Gambling it is otherwise. Not only have a variety\nof interesting single problems been discussed (of which the\nPetersburg problem is the best known) but several speculative\nquestions of considerable importance have been raised.\nOne of these concerns the disadvantages of the practice of\ngambling. There have been a number of writers who, not\ncontent with dwelling upon the obvious moral and indirect\nmischief which results, in the shape of over-excitement,\nconsequent greed, withdrawal from the steady business\nhabits which alone insure prosperity in the long run, diversion\nof wealth into dishonest hands, &c., have endeavoured\nto demonstrate the necessary loss caused by the practice.\n\n12. These attempts may be divided into two classes.\nThere are (1) those which appeal to merely numerical considerations,\nand (2) those which introduce what is called the\n'moral' as distinguished from the mathematical value of a\nfuture contingency.\n\n(1) For instance, an ingenious attempt has been made\nby Mr Whitworth to prove that gambling is necessarily\ndisadvantageous on purely mathematical grounds.\n\nWhen two persons play against each other one of the two\nmust be ruined sooner or later, even though the game be a\nfair one, supposing that they go on playing long enough; the\none with the smaller income having of course the worst\nchance of being the lucky survivor. If one of them has a\nfinite, and the other an infinite income, it must clearly be\nthe former who will be the ultimate sufferer if they go on\nlong enough. It is then maintained that this is in fact every\nindividual gambler's position, \"no one is restricted to gambling\nwith one single opponent; the speculator deals with the\npublic at large, with a world whose resources are practically\nunlimited. There is a prospect that his operations may\nterminate to his own disadvantage, through his having nothing\nmore to stake; but there is no prospect that it will\nterminate to his advantage through the exhaustion of the\nresources of the world. Every one who gambles is carrying\non an unequal warfare: he is ranged with a restricted capital\nagainst an adversary whose means are infinite.\"[7]\n\nIn the above argument it is surely overlooked that the\nadversaries against whom he plays are not one body with a\ncommon purse, like the bank in a gambling establishment.\nEach of these adversaries is in exactly the same position as\nhe himself is, and a precisely similar proof might be employed\nto show that each of them must be eventually ruined\nwhich is of course a reduction to absurdity. Gambling can\nonly transfer money from one player to another, and therefore\nnone of it can be actually lost.\n\n13. What really becomes of the money, when they\nplay to extremity, is not difficult to see. First suppose a\nlimited number of players. If they go on long enough, the\nmoney will at last all find its way into the pocket of some\none of their number. If their fortunes were originally equal,\neach stands the same chance of being the lucky survivor;\nin which case we cannot assert, on any numerical grounds,\nthat the prospect of the play is disadvantageous to any one\nof them. If their fortunes were unequal, the one who had\nthe largest sum to begin with can be shown to have the\nbest chance, according to some assignable law, of being left\nthe final winner; in which case it must be just as advantageous\nfor him, as it was disadvantageous for his less wealthy\ncompetitors.\n\nWhen, instead of a limited number of players, we suppose\nan unlimited number, each as he is ruined retiring\nfrom the table and letting another come in, the results are\nmore complicated, but their general tendency can be readily\ndistinguished. If we supposed that no one retired except\nwhen he was ruined, we should have a state of things in\nwhich all the old players were growing gradually richer. In\nthis case the prospect before the new comers would steadily\ngrow worse and worse, for their chance of winning against\nsuch rich opponents would be exceedingly small. But as\nthis is an unreasonable supposition, we ought rather to\nassume that not only do the ruined victims retire, but also\nthat those who have gained fortunes of a certain amount\nretire also, so that the aggregate and average wealth of the\ngambling body remains pretty steady. What chance any\ngiven player has of being ruined, and how long he may\nexpect to hold out before being ruined, will depend of course\nupon the initial incomes of the players, the rules of the\ngame, the stakes for which they play, and other considerations.\nBut it is clear that for all that is lost by one, a\nprecisely equal sum must be gained by others, and that\ntherefore any particular gambler can only be cautioned beforehand\nthat his conduct is not to be recommended, by\nappealing to some such suppositions as those already mentioned\nin a former section.\n\n14. As an additional justification of this view the\nreader may observe that the state of things in the last\nexample is one which, expressed in somewhat different\nlanguage and with a slight alteration of circumstances, is\nbeing incessantly carried on upon a gigantic scale upon\nevery side of us. Call it the competition of merchants and\ntraders in a commercial country, and the general results are\nfamiliar enough. It is true that in so far as skill comes into\nthe question, they are not properly gamblers; but in so far\nas chance and risk do, they may be fairly so termed, and in\nmany branches of business this must necessarily be the case\nto a very considerable extent. Whenever business is carried\non in a reckless way, the comparison is on general grounds\nfair enough. In each case alike we find some retiring ruined,\nand some making their fortunes; and in each case alike\nalso the chances, _coeteris paribus_, lie with those who have\nthe largest fortunes. Every one is, in a sense, struggling\nagainst the collective commercial world, but since each of his\ncompetitors is doing the same, we clearly could not caution\nany of them (except indeed the poorer ones) that their efforts\nmust finally end in disadvantage.\n\n15. If we wish to see this result displayed in its\nmost decisive form we may find a good analogy in a very\ndifferent class of events, viz. in the fate of _surnames_. We\nare all gamblers in this respect, and the game is carried\nout to the last farthing with a rigour unknown at Newmarket\nor Monte Carlo. In its complete treatment the\nsubject is a very intricate one,[8] but a simple example will\nserve to display the general tendency. Suppose a colony\ncomprising 1000 couples of different surnames, and suppose\nthat each of these has four children who grow up to marry.\nApproximately, one in 16 of these families will consist of\ngirls only; and therefore, under ordinary conventions, about\n62 of the names will have disappeared for ever after the\nnext generation. Four again out of 16 will have but one\nboy, each of whom will of course be in the same position\nas his father, viz. the sole representative of his name.\nAccordingly in the next generation one in 16 of these names\nwill again drop out, and so the process continues. The\nnumber which disappears in each successive generation becomes\nsmaller, as the stability of the survivors becomes\ngreater owing to their larger numbers. But there is no\ncheck to the process.\n\n16. The analogy here is a very close one, the names\nwhich thus disappear corresponding to the gamblers who\nretire ruined and those which increase in number corresponding\nto the lucky winners. The ultimate goal in each\ncase alike,--of course an exceedingly remote one,--is the\nexclusive survival of one at the expense of all the others.\nThat one surname does thus drop out after another must\nhave struck every one who has made any enquiry into family\ngenealogy, and various fanciful accounts have been given\nby those unfamiliar with the theory of probability. What\nis often apt to be overlooked is the extreme slightness of\nwhat may be termed the \"turn of the tables\" in favour\nof the survival at each generation. In the above numerical\nexample we have made an extravagantly favourable supposition,\nby assuming that the population doubles at every\ngeneration. In an old and thickly populated country where\nthe numbers increase very slowly, we should be much nearer\nthe mark in assuming that the average effective family,--that\nis, the average number of children who live to marry,--was\nonly _two_. In this case every family which was represented\nat any time by but a single male would have but\nthree chances in four of surviving extinction, and of course\nthe process of thinning out would be a more rapid one.\n\n17. The most interesting class of attempts to prove\nthe disadvantages of gambling appeal to what is technically\ncalled 'moral expectation' as distinguished from\n'mathematical expectation.' The latter may be defined\nsimply as the average money value of the venture in\nquestion; that is, it is the product of the amount to be\ngained (or lost) and the chance of gaining (or losing) it.\nFor instance, if I bet four to one in sovereigns against the\noccurrence of ace with a single die there would be, on the\naverage of many throws, a loss of four pounds against a gain\nof five pounds on each set of six occurrences; i.e. there\nwould be an average gain of three shillings and fourpence\non each throw. This is called the true or mathematical\nexpectation. The so-called 'moral expectation', on the other\nhand, is the subjective value of this mathematical expectation.\nThat is, instead of reckoning a money fortune in\nthe ordinary way, as what it _is_, the attempt is made to\nreckon it at what it is _felt_ to be. The elements of computation\ntherefore become, not pounds and shillings, but sums\nof pleasure enjoyed actually or in prospect. Accordingly\nwhen reckoning the present value of a future gain, we must\nnow multiply, not the objective but the subjective value,\nby the chance we have of securing that gain.\n\nWith regard to the exact relation of this moral fortune\nto the physical various more or less arbitrary assumptions\nhave been made. One writer (Buffon) considers that the\nmoral value of any given sum varies inversely with the\ntotal wealth of the person who gains it. Another (D. Bernoulli)\nstarting from a different assumption, which we shall\npresently have to notice more particularly, makes the moral\nvalue of a fortune vary as the logarithm of its actual amount.[9]\nA third (Cramer) makes it vary with the square root of the\namount.\n\n18. Historically, these proposals have sprung from\nthe wish to reconcile the conclusions of the Petersburg\nproblem with the dictates of practical common sense; for,\nby substituting the moral for the physical estimate the\ntotal value of the expectation could be reduced to a finite\nsum. On this ground therefore such proposals have no great\ninterest, for, as we have seen, there is no serious difficulty in\nthe problem when rightly understood.\n\nThese same proposals however have been employed in\norder to prove that gambling is necessarily disadvantageous,\nand this to both parties. Take, for instance, Bernoulli's supposition.\nIt can be readily shown that if two persons each\nwith a sum of \u00a350 to start with choose to risk, say, \u00a310 upon\nan even wager there will be a loss of happiness as a result;\nfor the pleasure gained by the possessor of \u00a360 will not\nbe equal to that which is lost by the man who leaves off\nwith \u00a340.[10]\n\n19. This is the form of argument commonly adopted;\nbut, as it stands, it does not seem conclusive. It may surely\nbe replied that all which is thus proved is that _inequality_ is\nbad, on the ground that two fortunes of \u00a350 are better than\none of \u00a360 and one of \u00a340. Conceive for instance that the\noriginal fortunes had been \u00a360 and \u00a340 respectively, the\nevent may result in an increase of happiness; for this will\ncertainly be the case if the richer man loses and the fortunes\nare thus equalized. This is quite true; and we are therefore\nobliged to show,--what can be very easily shown,--that if\nthe other alternative had taken place and the two fortunes\nhad been made still more unequal (viz. \u00a365 and \u00a335 respectively)\nthe happiness thus lost would more than balance\nwhat would have been gained by the equalization. And\nsince these two suppositions are equally likely there will be a\nloss in the long run.\n\nThe consideration just adduced seems however to show\nthat the common way of stating the conclusion is rather\nmisleading; and that, on the assumption in question as\nto the law of dependence of happiness on wealth, it really is\nthe case that the effective element in rendering gambling\ndisadvantageous is its tendency to the increase of the inequality\nin the distribution of wealth.\n\n20. This raises two questions, one of some speculative\ninterest in connection with our subject, and the other of\nsupreme importance in the conduct of life. The first is this:\nquite apart from any particular assumption which we make\nabout moral fortunes or laws of variation of happiness, is\nit the fact that gambling tends to increase the existing\ninequalities of wealth? Theoretically there is no doubt that\nthis is so. Take the simplest case and suppose two people\ntossing for a pound. If their fortunes were equal to begin\nwith there must be resultant inequality. If they were\nunequal there is an even chance of the inequality being\nincreased or diminished; but since the increase is proportionally\ngreater than the decrease, the final result remains of\nthe same kind as when the fortunes were equal.[11] Taking a\nmore general view the same conclusion underlies all our\nreasoning as to the averages of large numbers, viz. that the\nresultant divergencies increase absolutely (however they\ndiminish relatively) as the numbers become greater. And of\ncourse we refer to these absolute divergencies when we\nare talking of the distribution of wealth.\n\n21. This is the theoretic conclusion. How far the\nactual practice of gambling introduces counteracting agencies\nmust be left to the determination of those who are competent\nto pronounce. So far as outsiders are authorised\nto judge from what they read in the newspapers and other\npublic sources of information, it would appear that these\ncounteracting agencies are very considerable, and that in\nconsequence it is a rather insecure argument to advance\nagainst gambling. Many a large fortune has notoriously\nbeen squandered on the race-course or in gambling saloons,\nand most certainly a large portion, if not the major part,\nhas gone to swell the incomes of many who were by comparison\npoor. But the solution of this question must clearly be\nleft to those who have better opportunities of knowing\nthe facts than is to be expected on the part of writers on\nProbability.\n\n22. The general conclusion to be drawn is that those\nwho invoked this principle of moral fortune as an argument\nagainst gambling were really raising a much more intricate\nand far-reaching problem than they were aware of. What\nthey were at work upon was the question, What is the\ndistribution of wealth which tends to secure the maximum\nof happiness? Is this best secured by equality or inequality?\nHad they really followed out the doctrine on which their\ndenunciation of gambling was founded they ought to have\nadopted the Socialist's ideal as being distinctly that which\ntends to increase happiness. And they ought to have\nbrought under the same disapprobation which they expressed\nagainst gambling all those tendencies of modern\ncivilized life which work in the same direction. For instance;\nkeen competition, speculative operations, extended\nfacilities of credit, mechanical inventions, enlargement of\nbusiness operations into vast firms:--all these, and other\nsimilar tendencies too numerous to mention here, have had\nsome influence in the way of adding to existing inequalities.\nThey are, or have been, in consequence denounced by\nsocialists: are we honestly to bring them to this test in\norder to ascertain whether or not they are to be condemned?\nThe reader who wishes to see what sort of problems this\nassumption of 'moral fortune' ought to introduce may be\nrecommended to read Mr F. Y. Edgeworth's _Mathematical\nPsychics_, the only work with which I am acquainted which\ntreats of these questions.\n\n\n1. The question of the advisability of inoculation against the\n  small-pox, which gave rise to much discussion amongst the writers on\n  Probability during the last century, is a case in point of the same\n  principles applied to a very different kind of instance. The loss\n  against which the insurance was directed was death by small-pox, the\n  premium paid was the illness and other inconvenience, and the very\n  small risk of death, from the inoculation. The disputes which thence\n  arose amongst writers on the subject involved the same difficulties\n  as to the balance between certain moderate loss and contingent great\n  loss. In the seventeenth century it seems to have been an occasional\n  practice, before a journey into the Mediterranean, to insure against\n  capture by Moorish pirates, with a view to secure having the ransom\n  paid. (See, for an account of some extraordinary developments of the\n  insurance principle, Walford's _Insurance Guide and Handbook_. It is\n  not written in a very scientific spirit, but it contains much\n  information on all matters connected with insurance.)\n\n2. All that is meant by the above comparison is that the ideal aimed\n  at by Communism is similar to that of Insurance. If we look at the\n  processes by which it would be carried out, and the means for\n  enforcing it, the matter would of course assume a very different\n  aspect. Similarly with the action of Trades Unionism referred to in\n  the next paragraph.\n\n3. One of the best discussions that I have recently seen on these\n  subjects, by a writer at once thoroughly competent and well\n  informed, is in Mr Proctor's _Chance and Luck_. It appears to me\n  however that he runs into an extreme in his denunciation not of the\n  folly but of the dishonesty of all gambling. Surely also it is a\n  strained use of language to speak of all lotteries as 'unfair' and\n  even 'swindling' on the ground that the sum-total of what they\n  distribute in prizes is less than that of what they receive in\n  payments. The difference, in respect of information deliberately\n  withheld and false reports wilfully spread, between most of the\n  lotteries that have been supported, and the bubble companies which\n  justly deserve the name of swindles, ought to prevent the same name\n  being applied to both.\n\n4. \"A fire insurance is a simple bet between the office and the party,\n  and a life insurance is a collection of wagers. There is something\n  of the principle of a wager in every transaction in which the\n  results of a future event are to bring gain or loss.\" _Penny\n  Cyclop\u00e6dia_, under the head of _Wager_.\n\n5. _Encyclop\u00e9die Methodique_, under the head of _Tontines_.\n\n6. Of course, if we introduce considerations of Political Economy,\n  corrections will have to be made. For one thing, every Insurance\n  Office is, as De Morgan repeatedly insists, a _Savings Bank_ as well\n  as an Insurance Office. The Office invests the premiums, and can\n  therefore afford to pay a larger sum than would otherwise be the\n  case. Again, in the case of gambling, a large loss of capital by any\n  one will almost necessarily involve an actual destruction of wealth;\n  to say nothing of the fact that, practically, gambling often causes\n  a constant transfer of wealth from productive to unproductive\n  purposes.\n\n7. _Choice and Chance_, Ed. II. p. 208.\n\n8. It was, I believe, first treated as a serious problem by Mr Galton.\n  (See the _Journal Anthrop. Inst._ Vol. IV. 1875, where a complete\n  mathematical solution is indicated by Mr H. W. Watson.)\n\n9. Bernoulli himself does not seem to have based his conclusions upon\n  actual experience. But it is a noteworthy fact that the assumption\n  with which he starts, viz. that the subjective value of any small\n  increment (dx) is inversely proportional to the sum then possessed\n  (x), and which leads at once to the logarithmic law above mentioned,\n  is identical with one which is now familiar enough to every\n  psychologist. It is what is commonly called Fechner's Law, which he\n  has established by aid of an enormous amount of careful experiment\n  in the case of a number of our simple sensations. But I do not\n  believe that he has made any claim that such a law holds good in the\n  far more intricate dependence of happiness upon wealth.\n\n10. The formula expressive of this moral happiness is c log x/a; where\n  x stands for the physical fortune possessed at the time, and a for\n  that small value of it at which happiness is supposed to disappear:\n  c being an arbitrary constant. Let two persons, whose fortune is x,\n  risk y on an even bet. Then the balance, as regards happiness, must\n  be drawn between\n  c log x/a    and    1/2c log (x + y)/a + 1/2c log (x - y)/a,\n  or    log x^{2} and log(x + y)(x - y),\n  or    x^{2} and x^{2} - y^{2},\n  the former of which is necessarily the greater.\n\n11. This may be seen more clearly as follows. Suppose two pair of\n  gamblers, each pair consisting of men possessing \u00a350 and \u00a330\n  respectively. Now if we suppose the richer man to win in one case\n  and the poorer in the other these two results will be a fair\n  representation of the average; for there are only two alternatives\n  and these will be equally frequent in the long run. It is obvious\n  that we have had two fortunes of \u00a350 and two of \u00a330 converted into\n  one of \u00a320, two of \u00a340, and one of \u00a360. And this is clearly an\n  increase of inequality.\n\n\n\n\nCHAPTER XVI.\n\n\n_THE APPLICATION OF PROBABILITY TO TESTIMONY._\n\n1. On the principles which have been adopted in this\nwork, it becomes questionable whether several classes of\nproblems which may seem to have acquired a prescriptive\nright to admission, will not have to be excluded from the\nscience of Probability. The most important, perhaps, of\nthese refer to what is commonly called the credibility of\ntestimony, estimated either at first hand and directly, or as\ninfluencing a juryman, and so reaching us through his\nsagacity and trustworthiness. Almost every treatise upon\nthe science contains a discussion of the principles according\nto which credit is to be attached to combinations of the\nreports of witnesses of various degrees of trustworthiness, or\nthe verdicts of juries consisting of larger or smaller numbers.\nA great modern mathematician, Poisson, has written an\nelaborate treatise expressly upon this subject; whilst a considerable\nportion of the works of Laplace, De Morgan, and\nothers, is devoted to an examination of similar enquiries. It\nwould be presumptuous to differ from such authorities as\nthese, except upon the strongest grounds; but I confess that\nthe extraordinary ingenuity and mathematical ability which\nhave been devoted to these problems, considered as questions\nin Probability, fails to convince me that they ought to have\nbeen so considered. The following are the principal grounds\nfor this opinion.\n\n2. It will be remembered that in the course of the\nchapter on Induction we entered into a detailed investigation\nof the process demanded of us when, instead of the\nappropriate propositions from which the inference was to be\nmade being set before us, the _individual_ presented himself,\nand the task was imposed upon us of selecting the requisite\ngroups or series to which to refer him. In other words, instead\nof calculating the chance of an event from determinate\nconditions of frequency of its occurrence (these being either\nobtained by direct experience, or deductively inferred) we\nhave to _select_ the conditions of frequency out of a plurality\nof more or less suitable ones. When the problem is presented\nto us at such a stage as this, we may of course assume\nthat the preliminary process of obtaining the statistics\nwhich are extended into the proportional propositions has\nbeen already performed; we may suppose therefore that we\nare already in possession of a quantity of such propositions,\nour principal remaining doubt being as to which of them\nwe should then employ. This selection was shown to be\nto a certain extent arbitrary; for, owing to the fact of the\nindividual possessing a large number of different properties,\nhe became in consequence a member of different series or\ngroups, which might present different averages. We must\nnow examine, somewhat more fully than we did before,\nthe practical conditions under which any difficulty arising\nfrom this source ceases to be of importance.\n\n3. One condition of this kind is very simple and obvious.\nIt is that the different statistics with which we are\npresented should not in reality offer materially different\nresults, If, for instance, we were enquiring into the probability\nof a man aged forty dying within the year, we might\nif we pleased take into account the fact of his having red\nhair, or his having been born in a certain county or town.\nEach of these circumstances would serve to specialize the\nindividual, and therefore to restrict the limits of the statistics\nwhich were applicable to his case. But the consideration of\nsuch qualities as these would either leave the average precisely\nas it was, or produce such an unimportant alteration\nin it as no one would think of taking into account. Though\nwe could hardly say with certainty of any conceivable\ncharacteristic that it has absolutely no bearing on the\nresult, we may still feel very confident that the bearing of\nsuch characteristics as these is utterly insignificant. Of\ncourse in the extreme case of the things most perfectly\nsuited to the Calculus of Probability, viz. games of pure\nchance, these subsidiary characteristics are quite irrelevant.\nAny further particulars about the characteristics of the cards\nin a really fair pack, beyond those which are familiar to all\nthe players, would convey no information whatever about the\nresult.\n\nOr again; although the different sets of statistics may\nnot as above give almost identical results, yet they may do\nwhat practically comes to very much the same thing, that\nis, arrange themselves into a small number of groups, all of\nthe statistics in any one group practically coinciding in their\nresults. If for example a consumptive man desired to insure\nhis life, there would be a marked difference in the statistics\naccording as we took his peculiar state of health into account\nor not. We should here have two sets of statistics, so clearly\nmarked off from one another that they might almost rank\nwith the distinctions of natural kinds, and which would in\nconsequence offer decidedly different results. If we were\nto specialize still further, by taking into account insignificant\nqualities like those mentioned in the last paragraph, we\nmight indeed get more limited sets of statistics applicable\nto persons still more closely resembling the individual in\nquestion, but these would not differ sufficiently in their\nresults to make it worth our while to do so. In other words,\nthe different propositions which are applicable to the case in\npoint arrange themselves into a limited number of groups,\nwhich, and which only, need be taken into account; whence\nthe range of choice amongst them is very much diminished\nin practice.\n\n4. The reasons for the conditions above described are\nnot difficult to detect. Where these conditions exist the\nprocess of selecting a series or class to which to refer any\nindividual is very simple, and the selection is, for the particular\npurposes of inference, final. In any case of insurance,\nfor example, the question we have to decide is of the very\nsimple kind; Is A. B. a man of a certain age? If so one in\nfifty in his circumstances will die in the course of the year.\nIf any further questions have to be decided they would be of\nthe following description. Is A. B. a healthy man? Does he\nfollow a dangerous trade? But here too the classes in\nquestion are but few, and the limits by which they are\nbounded are tolerably precise; so that the reference of an\nindividual to one or other of them is easy. And when we\nhave once chosen our class we remain untroubled by any\nfurther considerations; for since no other statistics are supposed\nto offer a materially different average, we have no\noccasion to take account of any other properties than those\nalready noticed.\n\nThe case of games of chance, already referred to, offers\nof course an instance of these conditions in an almost ideal\nstate of perfection; the same circumstances which fit them\nso eminently for the purposes of fair gambling, fitting them\nequally to become examples in Probability. When a die is\nto be thrown, all persons alike stand on precisely the same\nfooting of knowledge and of ignorance about the result; the\nonly data to which any one could appeal being that each\nface turns up on an average once in six times.\n\n5. Let us now examine how far the above conditions\nare fulfilled in the case of problems which discuss what is\ncalled the credibility of testimony. The following would be\na fair specimen of one of the elementary enquiries out of\nwhich these problems are composed;--Here is a statement\nmade by a witness who lies once in ten times, what am I to\nconclude about its truth? Objections might fairly be raised\nagainst the possibility of thus assigning a man his place\nupon a graduated scale of mendacity. This however we will\npass over, and will assume that the witness goes about the\nworld bearing stamped somehow on his face the appropriate\nclass to which he belongs, and consequently, the degree of\ncredit to which he has a claim on such general grounds.\nBut there are other and stronger reasons against the admissibility\nof this class of problems.\n\n6. That which has been described in the previous\nsections as the 'individual' which had to be assigned to an\nappropriate class or series of statistics is, of course, in this\ncase, _a statement_. In the particular instance in question this\nindividual statement is already assigned to a class, that\nnamely of statements made by a witness of a given degree of\nveracity; but it is clearly optional with us whether or not we\nchoose to confine our attention to this class in forming our\njudgment; at least it would be optional whenever we were\npractically called on to form an opinion. But in the case of\nthis statement, as in that of the mortality of the man whose\ninsurance we were discussing, there are a multitude of other\nproperties observable, besides the one which is supposed to\nmark the given class. Just as in the latter there were\n(besides his age), the place of his birth, the nature of his\noccupation, and so on; so in the former there are (besides its\nbeing a statement by a certain kind of witness), the fact of its\nbeing uttered at a certain time and place and under certain\ncircumstances. At the time the statement is made all these\nqualities or attributes of the statement are present to us, and\nwe clearly have a right to take into account as many of them\nas we please. Now the question at present before us seems to\nbe simply this;--Are the considerations, which we might thus\nintroduce, as immaterial to the result in the case of the truth\nof a statement of a witness, as the corresponding considerations\nare in the case of the insurance of a life? There can\nsurely be no hesitation in the reply to such a question.\nUnder ordinary circumstances we soon know all that we can\nknow about the conditions which determine us in judging of\nthe prospect of a man's death, and we therefore rest content\nwith general statistics of mortality; but no one who heard a\nwitness speak would think of simply appealing to his figure\nof veracity, even supposing that this had been authoritatively\ncommunicated to us. The circumstances under which the\nstatement is made instead of being insignificant, are of overwhelming\nimportance. The appearance of the witness, the\ntone of his voice, the fact of his having objects to gain,\ntogether with a countless multitude of other circumstances\nwhich would gradually come to light as we reflect upon the\nmatter, would make any sensible man discard the assigned\naverage from his consideration. He would, in fact, no more\nthink of judging in this way than he would of appealing to\nthe Carlisle or Northampton tables of mortality to determine\nthe probable length of life of a soldier who was already in\nthe midst of a battle.\n\n7. It cannot be replied that under these circumstances\nwe still refer the witness to a class, and judge of his veracity\nby an average of a more limited kind; that we infer, for example,\nthat of men who look and act like him under such\ncircumstances, a much larger proportion, say nine-tenths,\nare found to lie. There is no appeal to a class in this way at\nall, there is no immediate reference to statistics of any kind\nwhatever; at least none which we are conscious of using at\nthe time, or to which we should think of resorting for justification\nafterwards. The decision seems to depend upon the\nquickness of the observer's senses and of his apprehension\ngenerally.\n\nStatistics about the veracity of witnesses seem in fact to\nbe permanently as inappropriate as all other statistics occasionally\nmay be. We may know accurately the percentage\nof recoveries after amputation of the leg; but what surgeon\nwould think of forming his judgment solely by such tables\nwhen he had a case before him? We need not deny, of\ncourse, that the opinion he might form about the patient's\nprospects of recovery might ultimately rest upon the proportions\nof deaths and recoveries he might have previously witnessed.\nBut if this were the case, these data are lying, as\none may say, obscurely in the background. He does not\nappeal to them directly and immediately in forming his\njudgment. There has been a far more important intermediate\nprocess of apprehension and estimation of what is\nessential to the case and what is not. Sharp senses, memory,\njudgment, and practical sagacity have had to be called into\nplay, and there is not therefore the same direct conscious\nand sole appeal to statistics that there was before. The\nsurgeon may have in his mind two or three instances in\nwhich the operation performed was equally severe, but in\nwhich the patient's constitution was different; the latter\nelement therefore has to be properly allowed for. There may\nbe other instances in which the constitution was similar, but\nthe operation more severe; and so on. Hence, although the\nultimate appeal may be to the statistics, it is not so directly;\ntheir value has to be estimated through the somewhat hazy\nmedium of our judgment and memory, which places them\nunder a very different aspect.\n\n8. Any one who knows anything of the game of whist\nmay supply an apposite example of the distinction here\ninsisted on, by recalling to mind the alteration in the nature\nof our inferences as the game progresses. At the commencement\nof the game our sole appeal is rightfully made to the\ntheory of Probability. All the rules upon which each player\nacts, and therefore upon which he infers that the others will\nact, rest upon the observed frequency (or rather upon the\nfrequency which calculation assures us will be observed) with\nwhich such and such combinations of cards are found to\noccur. Why are we told, if we have more than four trumps,\nto lead them out at once? Because we are convinced, on\npure grounds of probability, capable of being stated in the\nstrictest statistical form, that in a majority of instances we\nshall draw our opponent's trumps, and therefore be left with\nthe command. Similarly with every other rule which is\nrecognized in the early part of the play.\n\nBut as the play progresses all this is changed, and\ntowards its conclusion there is but little reliance upon any\nrules which either we or others could base upon statistical\nfrequency of occurrence, observed or inferred. A multitude\nof other considerations have come in; we begin to be influenced\npartly by our knowledge of the character and\npractice of our partner and opponents; partly by a rapid\ncombination of a multitude of judgments, founded upon\nour observation of the actual course of play, the grounds\nof which we could hardly realize or describe at the time\nand which may have been forgotten since. That is, the\nparticular combination of cards, now before us, does not\nreadily fall into any well-marked class to which alone it can\nreasonably be referred by every one who has the facts before\nhim.\n\n9. A criticism somewhat resembling the above has\nbeen given by Mill (_Logic,_ Bk. III. Chap. XVIII. \u00a73) upon\nthe applicability of the theory of Probability to the credibility\nof witnesses. But he has added other reasons which\ndo not appear to me to be equally valid; he says \"common\nsense would dictate that it is impossible to strike a general\naverage of the veracity, and other qualifications for true\ntestimony, of mankind or any class of them; and if it were\npossible, such an average would be no guide, the credibility of\nalmost every witness being either below or above the average,\"\nThe latter objection would however apply with equal force\nto estimating the length of a man's life from tables of mortality;\nfor the credibility of different witnesses can scarcely\nhave a wider range of variation than the length of different\nlives. If statistics of credibility could be obtained, and\ncould be conveniently appealed to when they were obtained,\nthey might furnish us in the long run with as accurate\ninferences as any other statistics of the same general description.\nThese statistics would however in practice naturally\nand rightly be neglected, because there can hardly fail\nto be circumstances in each individual statement which would\nmore appropriately refer it to some new class depending on\ndifferent statistics, and affording a far better chance of our\nbeing right in that particular case. In most instances of\nthe kind in question, indeed, such a change is thus produced\nin the mode of formation of our opinion, that, as already\npointed out, the mental operation ceases to be in any proper\nsense founded on appeal to statistics.[1]\n\n10. The Chance problems which are concerned with testimony\nare not altogether confined to such instances as those\nhitherto referred to. Though we must, as it appears to me,\nreject all attempts to estimate the credibility of any particular\nwitness, or to refer him to any assigned class in\nrespect of his trustworthiness, and consequently abandon as\nunsuitable any of the numerous problems which start from\nsuch data as 'a witness who is wrong once in ten times,'\nyet it does not follow that testimony may not to a slight\nextent be treated by our science in a somewhat different\nmanner. We may be quite unable to estimate, except in\nthe roughest possible way, the veracity of any particular\nwitness, and yet it may be possible to form some kind of\nopinion upon the veracity of certain classes of witnesses;\nto say, for instance, that Europeans are superior in this way\nto Orientals. So we might attempt to explain why, and to\nwhat extent, an opinion in which the judgments of ten persons,\nsay jurors, concur, is superior to one in which five only\nconcur. Something may also be done towards laying down\nthe principles in accordance with which we are to decide\nwhether, and why, extraordinary stories deserve less credence\nthan ordinary ones, even if we cannot arrive at any precise\nand definite decision upon the point. This last question is\nfurther discussed in the course of the next chapter.\n\n11. The change of view in accordance with which it\nfollows that questions of the kind just mentioned need not\nbe entirely rejected from scientific consideration, presents itself\nin other directions also. It has, for instance, been already\npointed out that the individual characteristics of any sick\nman's disease would be quite sufficiently important in most\ncases to prevent any surgeon from judging about his recovery\nby a genuine and direct appeal to statistics, however such\nconsiderations might indirectly operate upon his judgment.\nBut if an opinion had to be formed about a considerable\nnumber of cases, say in a large hospital, statistics might\nagain come prominently into play, and be rightly recognized\nas the principal source of appeal. We should feel able to\ncompare one hospital, or one method of treatment, with\nanother. The ground of the difference is obvious. It arises\nfrom the fact that the characteristics of the individuals,\nwhich made us so ready to desert the average when we had\nto judge of them separately, do not produce the same disturbance\nwhen were have to judge about a group of cases.\nThe averages then become the most secure and available\nground on which to form an opinion, and therefore Probability\nagain becomes applicable.\n\nBut although some resort to Probability may be admitted\nin such cases as these, it nevertheless does not\nappear to me that they can ever be regarded as particularly\nappropriate examples to illustrate the methods and resources\nof the theory. Indeed it is scarcely possible to resist the\nconviction that the refinements of mathematical calculation\nhave here been pushed to lengths utterly unjustifiable, when\nwe bear in mind the impossibility of obtaining any corresponding\ndegree of accuracy and precision in the data from\nwhich we have to start. To cite but one instance. It would\nbe hard to find a case in which love of consistency has prevailed\nover common sense to such an extent as in the admission\nof the conclusion that it is unimportant what are\nthe numbers for and against a particular statement, provided\nthe actual majority is the same. That is, the unanimous\njudgment of a jury of eight is to count for the same as a\nmajority of ten to two in a jury of twelve. And yet this\nconclusion is admitted by Poisson. The assumptions under\nwhich it follows will be indicated in the course of the next\nchapter.\n\nAgain, perfect independence amongst the witnesses or\njurors is an almost necessary postulate. But where can this\nbe secured? To say nothing of direct collusion, human\nbeings are in almost all instances greatly under the influence\nof sympathy in forming their opinions. This influence, under\nthe various names of political bias, class prejudice, local\nfeeling, and so on, always exists to a sufficient degree to\ninduce a cautious person to make many of those individual\ncorrections which we saw to be necessary when we were\nestimating the trustworthiness, in any given case, of a single\nwitness; that is, they are sufficient to destroy much, if not\nall, of the confidence with which we resort to statistics and\naverages in forming our judgment. Since then this Essay is\nmainly devoted to explaining and establishing the general\nprinciples of the science of Probability, we may very fairly\nbe excused from any further treatment of this subject, beyond\nthe brief discussions which are given in the next chapter.\n\n\n1. It may be remarked also that there is another reason which tends to\n  dissuade us from appealing to principles of Probability in the\n  majority of the cases where testimony has to be estimated. It often,\n  perhaps usually happens, that we are not absolutely forced to come\n  to a decision; at least so far as the acquitting of an accused\n  person may be considered as avoiding a decision. It may be of much\n  greater importance to us to attain not merely truth on the average,\n  but truth in each individual instance, so that we had rather not\n  form an opinion at all than form one of which we can only say in its\n  justification that it will tend to lead us right in the long run.\n\n\n\n\nCHAPTER XVII.\n\n\n_ON THE CREDIBILITY OF EXTRAORDINARY STORIES._\n\n1. It is now time to recur for fuller investigation to an\nenquiry which has been already briefly touched upon more\nthan once; that is, the validity of testimony to establish,\nas it is frequently expressed, an otherwise improbable story.\nIt will be remembered that in a previous chapter (the\ntwelfth) we devoted some examination to an assertion by\nButler, which seemed to be to some extent countenanced\nby Mill, that a great improbability before the proof might\nbecome but a very small improbability after the proof. In\nopposition to this it was pointed out that the different\nestimates which we undoubtedly formed of the credibility\nof the examples adduced, had nothing to do with the\nfact of the event being past or future, but arose from a\nvery different cause; that the conception of the event\nwhich we entertain at the moment (which is all that is then\nand there actually present to us, and as to the correctness\nof which as a representation of facts we have to make up our\nminds) comes before us in two very different ways. In one\ninstance it was a mere guess of our own which we knew\nfrom statistics would be right in a certain proportion of\ncases; in the other instance it was the assertion of a witness,\nand therefore the appeal was not now primarily to statistics of\nthe event, but to the trustworthiness of the witness. The conception,\nor 'event' if we will so term it, had in fact passed\nout of the category of guesses (on statistical grounds), into\nthat of assertions (most likely resting on some specific evidence),\nand would therefore be naturally regarded in a very\ndifferent light.\n\n2. But it may seem as if this principle would lead us\nto somewhat startling conclusions. For, by transferring the\nappeal from the frequency with which the event occurs to\nthe trustworthiness of the witness who makes the assertion,\nis it not implied that the probability or improbability of an\nassertion depends solely upon the veracity of the witness?\nIf so, ought not any story whatever to be believed when\nit is asserted by a truthful person?\n\nIn order to settle this question we must look a little\nmore closely into the circumstances under which such\ntestimony is commonly presented to us. As it is of course\nnecessary, for clearness of exposition, to take a numerical\nexample, let us suppose that a given statement is made by\na witness who, on the whole and in the long run, is right\nin what he says nine times out of ten.[1] Here then is an\naverage given to us, an average veracity that is, which\nincludes all the particular statements which the witness has\nmade or will make.\n\n3. Now it has been abundantly shown in a former\nchapter (Ch. IX. \u00a7\u00a714-32) that the mere fact of a particular\naverage having been assigned, is no reason for our\nbeing forced invariably to adhere to it, even in those cases\nin which our most natural and appropriate ground of judgment\nis found in an appeal to statistics and averages.\nThe general average may constantly have to be corrected\nin order to meet more accurately the circumstances of particular\ncases. In statistics of mortality, for instance; instead\nof resorting to the wider tables furnished by people in\ngeneral of a given age, we often prefer the narrower tables\nfurnished by men of a particular profession, abode, or mode\nof life. The reader may however be conveniently reminded\nhere that in so doing we must not suppose that we are able,\nby any such device, in any special or peculiar way to secure\ntruth. The general average, if persistently adhered to\nthroughout a sufficiently wide and varied experience, would\nin the long run tend to give us the truth; all the advantage\nwhich the more special averages can secure for us is to give\nus the same tendency to the truth with fewer and slighter\naberrations.\n\n4. Returning then to our witness, we know that if\nwe have a very great many statements from him upon all\npossible subjects, we may feel convinced that in nine out of\nten of these he will tell us the truth, and that in the tenth\ncase he will go wrong. This is nothing more than a matter\nof definition or consistency. But cannot we do better than\nthus rely upon his general average? Cannot we, in almost\nany given case, specialize it by attending to various characteristic\ncircumstances in the nature of the statement\nwhich he makes; just as we specialize his prospects of\nmortality by attending to circumstances in his constitution\nor mode of life?\n\nUndoubtedly we may do this; and in any of the practical\ncontingencies of life, supposing that we were at all guided\nby considerations of this nature, we should act very foolishly\nif we did not adopt some such plan. Two methods of thus\ncorrecting the average may be suggested: one of them being\nthat which practical sagacity would be most likely to employ,\nthe other that which is almost universally adopted by writers\non Probability. The former attempts to make the correction\nby the following considerations: instead of relying upon the\nwitness' general average, we assign to it a sort of conjectural\ncorrection to meet the case before us, founded on our experience\nor observation; that is, we appeal to experience to\nestablish that stories of such and such a kind are more or\nless likely to be true, as the case may be, than stories in\ngeneral. The other proceeds upon a different and somewhat\nmore methodical plan. It is here endeavoured to\nshow, by an analysis of the nature and number of the\nsources of error in the cases in question, that such and such\nkinds of stories must be more or less likely to be correctly\nreported, and this in certain numerical proportions.\n\n5. Before proceeding to a discussion of these methods\na distinction must be pointed out to which writers upon the\nsubject have not always attended, or at any rate to which\nthey have not generally sufficiently directed their readers'\nattention.[2] There are, broadly speaking, two different ways\nin which we may suppose testimony to be given. It may, in\nthe first place, take the form of a reply to an alternative\nquestion, a question, that is, framed to be answered by _yes_\nor _no_. Here, of course, the possible answers are mutually\ncontradictory, so that if one of them is not correct the other\nmust be so:--Has A happened, yes or no? The common\nmode of illustrating this kind of testimony numerically is by\nsupposing a lottery with a prize and blanks, or a bag of balls\nof two colours only, the witness knowing that there are only\ntwo, or at any rate being confined to naming one or other of\nthem. If they are black and white, and he errs when black\nis drawn, he must say 'white,' The reason for the prominence\nassigned to examples of this class is, probably, that\nthey correspond to the very important case of verdicts of\njuries; juries being supposed to have nothing else to do than\nto say 'guilty' or 'not guilty.'\n\nOn the other hand, the testimony may take the form of a\nmore original statement or piece of information. Instead of\nsaying, Did A happen? we may ask, What happened? Here\nif the witness speaks truth he must be supposed, as before,\nto have but one way of doing so; for the occurrence of some\nspecific event was of course contemplated. But if he errs he\nhas many ways of going wrong, possibly an infinite number.\nOrdinarily however his possible false statements are assumed\nto be limited in number, as must generally be more or less\nthe result in practice. This case is represented numerically\nby supposing the balls in the bag not to be of two colours\nonly, but to be all distinct from each other; say by their\nbeing all numbered successively. It may of course be objected\nthat a large number of the statements that are made\nin the world are not in any way answers to questions, either\nof the alternative or of the open kind. For instance, a man\nsimply asserts that he has drawn the seven of spades from a\npack of cards; and we do not know perhaps whether he had\nbeen asked 'Has that card been drawn?' or 'What card has\nbeen drawn?' or indeed whether he had been asked anything\nat all. Still more might this be so in the case of any ordinary\nhistorical statement.\n\nThis objection is quite to the point, and must be recognized\nas constituting an additional difficulty. All that we\ncan do is to endeavour, as best we may, to ascertain, from\nthe circumstances of the case, what number of alternatives\nthe witness may be supposed to have had before him. When\nhe simply testifies to some matter well known to be in dispute,\nand does not go much into detail, we may fairly consider\nthat there were practically only the two alternatives\nbefore him of saying 'yes' or 'no.' When, on the other hand,\nhe tells a story of a more original kind, or (what comes to\nmuch the same thing) goes into details, we must regard him\nas having a wide comparative range of alternatives before\nhim.\n\nThese two classes of examples, viz. that of the black and\nwhite balls, in which only one form of error is possible, and\nthe numbered balls, in which there may be many forms of\nerror, are the only two which we need notice. In practice it\nwould seem that they may gradually merge into each other,\naccording to the varying ways in which we choose to frame\nour question. Besides asking, Did you see A strike B? and,\nWhat did you see? we may introduce any number of intermediate\nleading questions, as, What did A do? What did\nhe do to B? and so on. In this way we may gradually narrow\nthe possible openings to wrong statement, and so approach\nto the direct alternative question. But it is clear that all\nthese cases may be represented numerically by a supposed\ndiminution in the number of the balls which are thus distinguished\nfrom each other.\n\n6. Of the two plans mentioned in \u00a74 we will begin\nwith the latter, as it is the only methodical and scientific one\nwhich has been proposed. Suppose that there is a bag with\n1000 balls, only one of which is white, the rest being all\nblack. A ball is drawn at random, and our witness whose\nveracity is 9/10 reports that the white ball was drawn. Take\na great many of his statements upon this particular subject,\nsay 10,000; that is, suppose that 10,000 balls having been\nsuccessively drawn out of this bag, or bags of exactly the\nsame kind, he makes his report in each case. His 10,000\nstatements being taken as a fair sample of his general average,\nwe shall find, by supposition, that 9 out of every 10 of\nthem are true and the remaining one false. What will be\nthe nature of these false statements? Under the circumstances\nin question, he having only one way of going wrong,\nthe answer is easy. In the 10,000 drawings the white ball\nwould come out 10 times, and therefore be rightly asserted\n9 times, whilst on the one of these occasions on which he\ngoes wrong he has nothing to say but 'black.' So with the\n9990 occasions on which black is drawn; he is right and\nsays black on 8991 of them, and is wrong and therefore says\nwhite on 999 of them. On the whole, therefore, we conclude\nthat out of every 1008 times on which he says that white is\ndrawn he is wrong 999 times and right only 9 times. That\nis, his special veracity, as we may term it, for cases of this\ndescription, has been reduced from 9/10 to 9/1008. As it would\ncommonly be expressed, the latter fraction represents the\nchance that this particular statement of his is true.[3]\n\n7. We will now take the case in which the witness\nhas many ways of going wrong, instead of merely one. Suppose\nthat the balls were all numbered, from 1 to 1,000, and\nthe witness knows this fact. A ball is drawn, and he tells\nme that it was numbered 25, what are the odds that he is\nright? Proceeding as before, in 10,000 drawings this ball\nwould be obtained 10 times, and correctly named 9 times.\nBut on the 9990 occasions on which it was not drawn there\nwould be a difference, for the witness has now many openings\nfor error before him. It is, however, generally considered\nreasonable to assume that his errors will all take the form of\nannouncing wrong numbers; and that, there being no apparent\nreason why he should choose one number rather than another,\nhe will be likely to announce all the wrong ones equally\noften. Hence his 999 errors, instead of all leading him now\nback again to one spot, will be uniformly spread over as\nmany distinct ways of going wrong. On one only of these\noccasions, therefore, will he mention 25 as having been\ndrawn. It follows therefore that out of every 10 times that\nhe names 25 he is right 9 times; so that in this case his\naverage or general truthfulness applies equally well to the\nspecial case in point.\n\n8. With regard to the truth of these conclusions, it\nmust of course be admitted that if we grant the validity of\nthe assumptions about the limits within which the blundering\nor mendacity of the witness are confined, and the complete\nimpartiality with which his answers are disposed within\nthose limits, the reasoning is perfectly sound. But are not\nthese assumptions extremely arbitrary, that is, are not our\nlotteries and bags of balls rendered perfectly precise in many\nrespects in which, in ordinary life, the conditions supposed to\ncorrespond to them are so vague and uncertain that no such\nmethod of reasoning becomes practically available? Suppose\nthat a person whom I have long known, and of whose measure\nof veracity and judgment I may be supposed therefore\nto have acquired some knowledge, informs me that there is\nsomething to my advantage if I choose to go to certain\ntrouble or expense in order to secure it. As regards the\ngeneral veracity of the witness, then, there is no difficulty;\nwe suppose that this is determined for us. But as regards\nhis story, difficulty and vagueness emerge at every point.\nWhat is the number of balls in the bag here? What in fact\nare the nature and contents of the bag out of which we suppose\nthe drawing to have been made? It does not seem\nthat the materials for any rational judgment exist here.\nBut if we are to get at any such amended figure of veracity\nas those attained in the above example, these questions must\nnecessarily be answered with some degree of accuracy; for\nthe main point of the method consists in determining how\noften the event must be considered _not_ to happen, and thence\ninferring how often the witness will be led wrongly to assert\nthat it has happened.\n\nIt is not of course denied that considerations of the kind\nin question have some influence upon our decision, but only\nthat this influence could under any ordinary circumstances\nbe submitted to numerical determination. We are doubtless\nliable to have information given to us that we have\ncome in for some kind of fortune, for instance, when no\nsuch good luck has really befallen us; and this not once\nonly but repeatedly. But who can give the faintest intimation\nof the nature and number of the occasions on which,\na blank being thus really drawn, a prize will nevertheless\nbe falsely announced? It appears to me therefore that\nnumerical results of any practical value can seldom, if ever,\nbe looked for from this method of procedure.\n\n9. Our conclusion in the case of the lottery, or, what\ncomes to the same thing, in the case of the bag with black\nand white balls, has been questioned or objected to[4] on the\nground that it is contrary to all experience to suppose that\nthe testimony of a moderately good witness could be so\nenormously depreciated under such circumstances. I should\nprefer to base the objection on the ground that experience\nscarcely ever presents such circumstances as those supposed;\nbut if we postulate their existence the given conclusion seems\ncorrect enough. Assume that a man is merely required to\nsay _yes_ or _no_; assume also a group or succession of cases in\nwhich _no_ should rightly be said very much oftener than\n_yes_. Then, assuming almost any general truthfulness of the\nwitness, we may easily suppose the rightful occasions for\ndenial to be so much the more frequent that a majority of\nhis affirmative answers will actually occur as false 'noes'\nrather than as correct 'ayes.' This of course lowers the\naverage value of his 'ayes,' and renders them comparatively\nuntrustworthy.\n\nConsider the following example. I have a gardener whom\nI trust as to all ordinary matters of fact. If he were to\ntell me some morning that my dog had run away I should\nfully believe him. He tells me however that the dog has\ngone mad. Surely I should accept the statement with much\nhesitation, and on the grounds indicated above. It is not\nthat he is more likely to be wrong when the dog _is_ mad;\nbut that experience shows that there are other complaints\n(e.g. fits) which are far more common than madness, and\nthat most of the assertions of madness are erroneous assertions\nreferring to these. This seems a somewhat parallel\ncase to that in which we find that most of the assertions\nthat a white ball had been drawn are really false assertions\nreferring to the drawing of a black ball. Practically I do\nnot think that any one would feel a difficulty in thus exorbitantly\ndiscounting some particular assertion of a witness\nwhom in most other respects he fully trusted.\n\n10. There is one particular case which has been regarded\nas a difficulty in the way of this treatment of the\nproblem, but which seems to me to be a decided confirmation\nof it; always, be it understood, within the very narrow\nand artificial limits to which we must suppose ourselves to\nbe confined. This is the case of a witness whose veracity is\njust one-half; that is, one who, when a mere _yes_ or _no_ is\ndemanded of him, is as often wrong as right. In the case of\nany other assigned degree of veracity it is extremely difficult\nto get anything approaching to a confirmation from practical\njudgment and experience. We are not accustomed to\nestimate the merits of witnesses in this way, and hardly appreciate\nwhat is meant by his numerical degree of truthfulness.\nBut as regards the man whose veracity is one-half, we\nare (as Mr C. J. Monro has very ingeniously suggested) only\ntoo well acquainted with such witnesses, though under a\nsomewhat different name; for this is really nothing else than\nthe case of a person confidently answering a question about\na subject-matter of which he knows nothing, and can therefore\nonly give a mere guess.\n\nNow in the case of the lottery with one prize, when the\nwitness whose veracity is one-half tells us that we have\ngained the prize, we find on calculation that his testimony\ngoes for absolutely nothing; the chances that we have got\nthe prize are just the same as they would be if he had never\nopened his lips, viz. 1/1000. But clearly this is what ought\nto be the result, for the witness who knows nothing about\nthe matter leaves it exactly as he found it. He is indeed,\nin strictness, scarcely a witness at all; for the natural function\nof a witness is to examine the matter, and so to add\nconfirmation, more or less, according to his judgment and\nprobity, but at any rate to offer an improvement upon the\nmere guesser. If, however, we will give heed to his mere\nguess we are doing just the same thing as if we were to guess\nourselves, in which case of course the odds that we are right\nare simply measured by the frequency of occurrence of the\nevents.\n\nWe cannot quite so readily apply the same rule to the\nother case, namely to that of the numbered balls, for there\nthe witness who is right every other time may really be a\nvery fair, or even excellent, witness. If he has many ways\nof going wrong, and yet is right in half his statements, it is\nclear that he must have taken some degree of care, and cannot\nhave merely guessed. In a case of _yes_ or _no_, any one can\nbe right every other time, but it is different where truth\nis single and error is manifold. To represent the case of a\nsimply worthless witness when there were 1000 balls and\nthe drawing of one assigned ball was in question, we should\nhave to put his figure of veracity at 1/1000. If this were\ndone we should of course get a similar result.\n\n11. It deserves notice therefore that the figure of\nveracity, or fraction representing the general truthfulness\nof a witness, is in a way relative, not absolute; that is, it\ndepends upon, and varies with, the general character of the\nanswer which he is supposed to give. Two witnesses of\nequal intrinsic veracity and worth, one of whom confined\nhimself to saying _yes_ and _no_, whilst the other ventured to\nmake more original assertions, would be represented by\ndifferent fractions; the former having set himself a much\neasier task than the latter. The real caution and truthfulness\nof the witness are only one factor, therefore, in his\nactual figure of veracity; the other factor consists of the\nnature of his assertions, as just pointed out. The ordinary\nplan therefore, in such problems, of assigning an average\ntruthfulness to the witness, and accepting this alike in the\ncase of each of the two kinds of answers, though convenient,\nseems scarcely sound. This consideration would however\nbe of much more importance were not the discussions upon\nthe subject mainly concerned with only one description of\nanswer, namely that of the 'yes or no' kind.\n\n12. So much for the methodical way of treating such\na problem. The way in which it would be taken in hand by\nthose who had made no study of Probability is very different.\nIt would, I apprehend, strike them as follows. They would\nsay to themselves, Here is a story related by a witness who\ntells the truth, say, nine times out of ten. But it is a story\nof a kind which experience shows to be very generally made\nuntruly, say 99 times out of 100. Having then these opposite\ninducements to belief, they would attempt in some way\nto strike a balance between them. Nothing in the nature of\na strict rule could be given to enable them to decide how\nthey might escape out of the difficulty. Probably, in so far\nas they did not judge at haphazard, they would be guided\nby still further resort to experience, or unconscious recollections\nof its previous teachings, in order to settle which\nof the two opposing inductions was better entitled to carry\nthe day in the particular case before them. The reader\nwill readily see that any general solution of the problem,\nwhen thus presented, is impossible. It is simply the now\nfamiliar case (Chap. IX. \u00a7\u00a714-32) of an individual which\nbelongs equally to two distinct, or even, in respect of their\ncharacteristics, opposing classes. We cannot decide off-hand\nto which of the two its characteristics most naturally and\nrightly refer it. A fresh induction is needed in order to\nsettle this point.\n\n13. Rules have indeed been suggested by various\nwriters in order to extricate us from the difficulty. The controversy\nabout miracles has probably been the most fertile\noccasion for suggestions of this kind on one side or the\nother. It is to this controversy, presumably, that the phrase\nis due, so often employed in discussions upon similar subjects,\n'a contest of opposite improbabilities.' What is meant\nby such an expression is clearly this: that in forming a\njudgment upon the truth of certain assertions we may find\nthat they are comprised in two very distinct classes, so that,\naccording as we regarded them as belonging to one or the\nother of these distinct classes, our opinion as to their truth\nwould be very different. Such an assertion belongs to one\nclass, of course, by its being a statement of a particular\nwitness, or kind of witness; it belongs to the other by its\nbeing a particular kind of story, one of what is called an\nimprobable nature. Its belonging to the former class is so\nfar favourable to its truth, its belonging to the latter is so far\nhostile to its truth. It seems to be assumed, in speaking of\na contest of opposite improbabilities, that when these different\nsources of conviction co-exist together, they would each in\nsome way retain their probative force so as to produce a\ncontest, ending generally in a victory to one or other of\nthem. Hume, for instance, speaks of our _deducting_ one\nprobability from the other, and apportioning our belief to\nthe remainder.[5] Thomson, in his _Laws of Thought_, speaks\nof one probability as entirely superseding the other.\n\n14. It does not appear to me that the slightest philosophical\nvalue can be attached to any such rules as these.\nThey doubtless may, and indeed will, hold in individual\ncases, but they cannot lay claim to any generality. Even\nthe notion of a contest, as any necessary ingredient in the\ncase, must be laid aside. For let us refer again to the way\nin which the perplexity arises, and we shall readily see, as\nhas just been remarked, that it is nothing more than a particular\nexemplification of a difficulty which has already been\nrecognized as incapable of solution by any general _\u00e0 priori_\nmethod of treatment. All that we are supposed to have before\nus is a statement. On this occasion it is made by a witness\nwho lies, say, once in ten times in the long run; that is, who\nmostly tells the truth. But on the other hand, it is a statement\nwhich experience, derived from a variety of witnesses on\nvarious occasions, assures us is mostly false; stated numerically\nit is found, let us suppose, to be false 99 times in a hundred.\n\nNow, as was shown in the chapter on Induction, we are\nthus brought to a complete dead lock. Our science offers no\nprinciples by which we can form an opinion, or attempt to\ndecide the matter one way or the other; for, as we found,\nthere are an indefinite number of conclusions which are all\nequally possible. For instance, all the witness' extraordinary\nassertions may be true, or they may all be false, or they may\nbe divided into the true and the false in any proportion\nwhatever. Having gone so far in our appeal to statistics as\nto recognize that the witness is generally right, but that his\nstory is generally false, we cannot stop there. We ought to\nmake still further appeal to experience, and ascertain how it\nstands with regard to his stories when they are of that\nparticular nature: or rather, for this would be to make a\nneedlessly narrow reference, how it stands with regard to\nstories of that kind when advanced by witnesses of his\ngeneral character, position, sympathies, and so on.[6]\n\n15. That extraordinary stories are in many cases, probably\nin a great majority of cases, less trustworthy than\nothers must be fully admitted. That is, if we were to make\ntwo distinct classes of such stories respectively, we should\nfind that the same witness, or similar witnesses, were proportionally\nmore often wrong when asserting the former than\nwhen asserting the latter. But it does not by any means\nappear to me that this must always be the case. We may\nwell conceive, for instance, that with some people the mere\nfact of the story being of a very unusual character may make\nthem more careful in what they state, so as actually to add\nto their veracity. If this were so we might be ready to\naccept their extraordinary stories with even more readiness\nthan their ordinary ones.\n\nSuch a supposition as that just made does not seem to me\nby any means forced. Put such a case as this: let us suppose\nthat two persons, one of them a man of merely ordinary\nprobity and intelligence, the other a scientific naturalist,\nmake a statement about some common event. We believe\nthem both. Let them now each report some extraordinary\n_lusus natur\u00e6_ or monstrosity which they profess to have seen.\nMost persons, we may presume, would receive the statement\nof the naturalist in this latter case almost as readily as in\nthe former: whereas when the same story came from the\nunscientific observer it would be received with considerable\nhesitation. Whence arises the difference? From the conviction\nthat the naturalist will be far more careful, and\ntherefore to the full as accurate, in matters of this kind as\nin those of the most ordinary description, whereas with the\nother man we feel by no means the same confidence. Even\nif any one is not prepared to go this length, he will probably\nadmit that the difference of credit which he would attach to\nthe two kinds of story, respectively, when they came from\nthe naturalist, would be much less than what it would be\nwhen they came from the other man.\n\n16. Whilst we are on this part of the subject, it must\nbe pointed out that there is considerable ambiguity and\nconsequent confusion about the use of the term 'an extraordinary\nstory.' Within the province of pure Probability it\nought to mean simply a story which asserts an _unusual_ event.\nAt least this is the view which has been adopted and maintained,\nit is hoped consistently, throughout this work. So\nlong as we adhere to this sense we know precisely what we\nmean by the term. It has a purely objective reference; it\nsimply connotes a very low degree of relative statistical\nfrequency, actual or prospective. Out of a great number of\nevents we suppose a selection of some particular kind to be\ncontemplated, which occurs relatively very seldom, and this\nis termed an unusual or extraordinary event. It follows, as\nwas abundantly shown in a former chapter, that owing to\nthe rarity of the event we are very little disposed to expect\nits occurrence in any given case. Our guess about it, in case\nwe thus anticipated it, would very seldom be justified, and\nwe are therefore apt to be much surprised when it does\noccur. This, I take it, is the only legitimate sense of 'extraordinary'\nso far as Probability is concerned.\n\nBut there is another and very different use of the word,\nwhich belongs to Induction, or rather to the science of\nevidence in general, more than to that limited portion of it\ntermed Probability. In this sense the 'extraordinary,' and\nstill more the 'improbable,' event is not merely one of\nextreme statistical rarity, which we could not expect to\nguess aright, but which on moderate evidence we may pretty\nreadily accept; it is rather one which possesses, so to say, an\nactual evidence-resisting power. It may be something which\naffects the credibility of the witness at the fountain-head,\nwhich makes, that is, his statements upon such a subject\nessentially inferior to those on other subjects. This is the\ncase, for instance, with anything which excites his prejudices\nor passions or superstitions. In these cases it would seem\nunreasonable to attempt to estimate the credibility of the\nwitness by calculating (as in \u00a76) how often his errors would\nmislead us through his having been wrongly brought to an\naffirmation instead of adhering correctly to a negation. We\nshould rather be disposed to put our correction on the witness'\naverage veracity at once.\n\n17. In true Probability, as has just been remarked,\nevery event has its own definitely recognizable degree of\nfrequency of occurrence. It may be excessively rare, rare to\nany extreme we like to postulate, but still every one who\nunderstands and admits the data upon which its occurrence\ndepends will be able to appreciate within what range of\nexperience it may be expected to present itself. We do not\nexpect it in any individual case, nor within any brief range,\nbut we do confidently expect it within an adequately extensive\nrange. How therefore can miraculous stories be similarly\ntaken account of, when the disputants, on one side at\nleast, are not prepared to admit their actual occurrence anywhere\nor at any time? How can any arrangement of bags\nand balls, or other mechanical or numerical illustrations of\nunlikely events, be admitted as fairly illustrative of miraculous\noccurrences, or indeed of many of those which come\nunder the designation of 'very extraordinary' or 'highly\nimprobable'? Those who contest the occurrence of a particular\nmiracle, as reported by this or that narrator, do not\nadmit that miracles are to be confidently expected sooner or\nlater. It is not a question as to whether what must happen\nsometimes has happened some particular time, and therefore\nno illustration of the kind can be regarded as apposite.\n\nHow unsuitable these merely rare events, however excessive\ntheir rarity may be, are as examples of miraculous\nevents, will be evident from a single consideration. No one,\nI presume, who admitted the occasional occurrence of an exceedingly\nunusual combination, would be in much doubt if\nhe considered that he had actually seen it himself.[7] On the\nother hand, few men of any really scientific turn would\nreadily accept a miracle even if it appeared to happen under\ntheir very eyes. They might be staggered at the time, but\nthey would probably soon come to discredit it afterwards,\nor so explain it as to evacuate it of all that is meant by\nmiraculous.\n\n18. It appears to me therefore, on the whole, that\nvery little can be made of these problems of testimony in\nthe way in which it is generally intended that they should\nbe treated; that is, in obtaining specific rules for the estimation\nof the testimony under any given circumstances.\nAssuming that the veracity of the witness can be measured,\nwe encounter the real difficulty in the utter impossibility of\ndetermining the limits within which the failures of the event\nin question are to be considered to lie, and the degree of\nexplicitness with which the witness is supposed to answer\nthe enquiry addressed to him; both of these being characteristics\nof which it is necessary to have a numerical estimate\nbefore we can consider ourselves in possession of the\nrequisite data.\n\nSince therefore the practical resource of most persons,\nviz. that of putting a direct and immediate correction, of\ncourse of a somewhat conjectural nature, upon the general\ntrustworthiness of the witness, by a consideration of the\nnature of the circumstances under which his statement is\nmade, is essentially unscientific and irreducible to rule; it\nreally seems to me that there is something to be said in\nfavour of the simple plan of trusting in all cases alike to\nthe witness' general veracity.[8] That is, whether his story\nis ordinary or extraordinary, we may resolve to put it on\nthe same footing of credibility, provided of course that the\nevent is fully recognized as one which does or may occasionally\nhappen. It is true that we shall thus go constantly\nastray, and may do so to a great extent, so that if there\nwere any rational and precise method of specializing his\ntrustworthiness, according to the nature of his story, we\nshould be on much firmer ground. But at least we may\nthus know what to expect on the average. Provided we\nhave a sufficient number and variety of statements from\nhim, and always take them at the same constant rate or\ndegree of trustworthiness, we may succeed in balancing and\ncorrecting our conduct in the long run so as to avoid any\nruinous error.\n\n19. A few words may now be added about the combination\nof testimony. No new principles are introduced here,\nthough the consequent complication is naturally greater. Let\nus suppose two witnesses, the veracity of each being 9/10.\nNow suppose 100 statements made by the pair; according to\nthe plan of proceeding adopted before, we should have them\nboth right 81 times and both wrong once, in the remaining\n18 cases one being right and the other wrong. But since\nthey are both supposed to give the same account, what we\nhave to compare together are the number of occasions on\nwhich they agree and are right, and the total number on which\nthey agree whether right or wrong. The ratio of the former\nto the latter is the fraction which expresses the trustworthiness\nof their combination of testimony in the case in question.\n\nIn attempting to decide this point the only difficulty is\nin determining how often they will be found to agree when\nthey are both wrong, for clearly they must agree when they\nare both right. This enquiry turns of course upon the number\nof ways in which they can succeed in going wrong.\nSuppose first the case of a simple _yes_ or _no_ (as in \u00a76), and\ntake the same example, of a bag with 1000 balls, in which\none only is white. Proceeding as before, we should find that\nout of 100,000 drawings (the number required in order to\nobtain a complete cycle of all possible occurrences, as well as\nof all possible reports about them) the two witnesses agree\nin a correct report of the appearance of white in 81, and\nagree in a wrong report of it in 999. The Probability therefore\nof the story when so attested is 81/1080; the fact therefore\nof two such witnesses of equal veracity having concurred\nmakes the report nearly 9 times as likely as when it rested\nupon the authority of only one of them.[9]\n\n20. When however the witnesses have many ways of\ngoing wrong, the fact of their agreeing makes the report far\nmore likely to be true. For instance, in the case of the 1000\nnumbered balls, it is very unlikely that when they both mistake\nthe number they should (without collusion) happen to\nmake the same misstatement. Whereas, in the last case,\nevery combined misstatement necessarily led them both to\nthe assertion that the event in question had happened, we\nshould now find that only once in 999 \u00d7 999 times would\nthey both be led to assert that _some given number_ (say, as\nbefore, 25) had been drawn. The odds in favour of the\nevent in fact now become 80919/80920, which are enormously\ngreater than when there was only one witness.\n\nIt appears therefore that when two, and of course still\nmore when many, witnesses agree in a statement in a matter\nabout which they might make many and various errors, the\ncombination of their favourable testimony adds enormously\nto the likelihood of the event; provided always that there\nis no chance of collusion. And in the extreme case of the\nopportunities for error being, as they well may be, practically\ninfinite in number, such combination would produce almost\nperfect certainty. But then this condition, viz. absence of\ncollusion, very seldom can be secured. Practically our main\nsource of error and suspicion is in the possible existence of\nsome kind of collusion. Since we can seldom entirely get\nrid of this danger, and when it exists it can never be submitted\nto numerical calculation, it appears to me that combination\nof testimony, in regard to detailed accounts, is yet\nmore unfitted for consideration in Probability than even that\nof single testimony.\n\n21. The impossibility of any adequate or even appropriate\nconsideration of the credibility of miraculous stories\nby the rules of Probability has been already noticed in \u00a717.\nBut, since the grounds of this impossibility are often very\ninsufficiently appreciated, a few pages may conveniently be\nadded here with a view to enforcing this point. If it be\nregarded as a digression, the importance of the subject and\nthe persistency with which various writers have at one time\nor another attempted to treat it by the rules of our science\nmust be the excuse for entering upon it.\n\nA necessary preliminary will be to decide upon some definition\nof a miracle. It will, we may suppose, be admitted by\nmost persons that in calling a miracle 'a suspension of a law\nof causation,' we are giving what, though it may not amount\nto an adequate definition, is at least true as a description.\nIt is true, though it may not be the whole truth. Whatever\nelse the miracle may be, this is its physical aspect: this is the\npoint at which it comes into contact with the subject-matter\nof science. If it were not considered that any suspension of\ncausation were involved, the event would be regarded merely\nas an ordinary one to which some special significance was\nattached, that is, as a type or symbol rather than a miracle.\nIt is this aspect moreover of the miracle which is now exposed\nto the main brunt of the attack, and in support of\nwhich therefore the defence has generally been carried on.\n\nNow it is obvious that this, like most other definitions or\ndescriptions, makes some assumption as to matters of fact,\nand involves something of a theory. The assumption clearly\nis, that laws of causation prevail universally, or almost universally,\nthroughout nature, so that infractions of them are\nmarked and exceptional. This assumption is made, but it\ndoes not appear that anything more than this is necessarily\nrequired; that is, there is nothing which need necessarily\nmake us side with either of the two principal schools which\nare divided as to the nature of these laws of causation. The\ndefinition will serve equally well whether we understand by\n_law_ nothing more than uniformity of antecedent and consequent,\nor whether we assert that there is some deeper and\nmore mysterious tie between the events than mere sequence.\nThe use of the term 'causation' in this minimum of signification\nis common to both schools, though the one might\nconsider it inadequate; we may speak, therefore, of 'suspensions\nof causation' without committing ourselves to either.\n\n22. It should be observed that the aspect of the question\nsuggested by this definition is one from which we can\nhardly escape. Attempts indeed have been sometimes made\nto avoid the necessity of any assumption as to the universal\nprevalence of law and order in nature, by defining a miracle\nfrom a different point of view. A miracle may be called, for\ninstance, 'an immediate exertion of creative power,' 'a sign\nof a revelation,' or, still more vaguely, an 'extraordinary\nevent.' But nothing would be gained by adopting any such\ndefinitions as these. However they might satisfy the theologian,\nthe student of physical science would not rest content\nwith them for a moment. He would at once assert his own\nbelief, and that of other scientific men, in the existence of\nuniversal law, and enquire what was the connection of the\ndefinition with this doctrine. An answer would imperatively\nbe demanded to the question, Does the miracle, as you have\ndescribed it, imply an infraction of one of these laws, or does\nit not? And an answer must be given, unless indeed we\nreject his assumption by denying our belief in the existence\nof this universal law, in which case of course we put ourselves\nout of the pale of argument with him. The necessity\nof having to recognize this fact is growing upon men day by\nday, with the increased study of physical science. And since\nthis aspect of the question has to be met some time or other,\nit is as well to place it in the front. The difficulty, in its\nscientific form, is of course a modern one, for the doctrine out\nof which it arises is modern. But it is only one instance, out\nof many that might be mentioned, in which the growth of\nsome philosophical conception has gradually affected the\nnature of the dispute, and at last shifted the position of the\nbattle-ground, in some discussion with which it might not at\nfirst have appeared to have any connection whatever.\n\n23. So far our path is plain. Up to this point disciples\nof very different schools may advance together; for in laying\ndown the above doctrine we have carefully abstained from\nimplying or admitting that it contains the whole truth. But\nfrom this point two paths branch out before us, paths as\ndifferent from each other in their character, origin, and\ndirection, as can well be conceived. As this enquiry is only\na digression, we may confine ourselves to stating briefly what\nseem to be the characteristics of each, without attempting to\ngive the arguments which might be used in their support.\n\n(I.) On the one hand, we may assume that this principle\nof causation is the ultimate one. By so terming it, we do\nnot mean that it is one from which we consciously start in\nour investigations, as we do from the axioms of geometry,\nbut rather that it is the final result towards which we find\nourselves drawn by a study of nature. Finding that,\nthroughout the scope of our enquiries, event follows event in\nnever-failing uniformity, and finding moreover (some might\nadd) that this experience is supported or even demanded by\na tendency or law of our nature (it does not matter here how\nwe describe it), we may come to regard this as the one\nfundamental principle on which all our enquiries should rest.\n\n(II.) Or, on the other hand, we may admit a class of\nprinciples of a very different kind. Allowing that there is\nthis uniformity so far as our experience extends, we may yet\nadmit what can hardly be otherwise described than by\ncalling it a Superintending Providence, that is, a Scheme or\nOrder, in reference to which Design may be predicated\nwithout using merely metaphorical language. To adopt an\naptly chosen distinction, it is not to be understood as _over-ruling_\nevents, but rather as _underlying_ them.\n\n24. Now it is quite clear that according as we come to\nthe discussion of any particular miracle or extraordinary\nstory under one or other of these prepossessions, the question\nof its credibility will assume a very different aspect. It\nis sometimes overlooked that although a difference about\n_facts_ is one of the conditions of a _bon\u00e2 fide_ argument, a difference\nwhich reaches to ultimate principles is fatal to all\nargument. The possibility of present conflict is banished in\nsuch a case as absolutely as that of future concord. A large\namount of popular literature on the subject of miracles\nseems to labour under this defect. Arguments are stated\nand examined for and against the credibility of miraculous\nstories without the disputants appearing to have any\nadequate conception of the chasm which separates one side\nfrom the other.\n\n25. The following illustration may serve in some\ndegree to show the sort of inconsistency of which we are\nspeaking. A sailor reports that in some remote coral island\nof the Pacific, on which he had landed by himself, he had\nfound a number of stones on the beach disposed in the exact\nform of a cross. Now if we conceive a debate to arise about\nthe truth of his story, in which it is attempted to decide the\nmatter simply by considerations about the validity of testimony,\nwithout introducing the question of the existence of\ninhabitants, and the nature of their customs, we shall have\nsome notion of the unsatisfactory nature of many of the\ncurrent arguments about miracles. All illustrations of this\nsubject are imperfect, but a case like this, in which a supposed\ntrace of human agency is detected interfering with the\norderly sequence of other and non-intelligent natural causes,\nis as much to the point as any illustration can be. The\nthing omitted here from the discussion is clearly the one important\nthing. If we suppose that there is no inhabitant, we\nshall probably disbelieve the story, or consider it to be\ngrossly exaggerated. If we suppose that there are inhabitants,\nthe question is at once resolved into a different and\nsomewhat more intricate one. The credibility of the witness\nis not the only element, but we should necessarily have to\ntake into consideration the character of the supposed inhabitants,\nand the object of such an action on their part.\n\n26. Considerations of this character are doubtless\noften introduced into the discussion, but it appears to me\nthat they are introduced to a very inadequate extent. It is\noften urged, after Paley, 'Once believe in a God, and miracles\nare not incredible.' Such an admission surely demands\nsome modification and extension. It should rather be stated\nthus, Believe in a God whose working may be traced throughout\nthe whole moral and physical world. It amounts, in\nfact, to this;--Admit that there may be a _design_ which we\ncan trace somehow or other in the course of things; admit\nthat we are not wholly confined to tracing the connection of\nevents, or following out their effects, but that we can form\nsome idea, feeble and imperfect though it be, of a _scheme_.[10]\nPaley's advice sounds too much like saying, Admit that there\nare fairies, and we can account for our cups being cracked.\nThe admission is not to be made in so off-hand a manner.\nTo any one labouring under the difficulty we are speaking\nof, this belief in a God almost out of any constant relation to\nnature, whom we then imagine to occasionally manifest himself\nin a perhaps irregular manner, is altogether impossible.\nThe only form under which belief in the Deity can gain entrance\ninto his mind is as the controlling Spirit of an infinite\nand orderly system. In fact, it appears to me, paradoxical\nas the suggestion may appear, that it might even be more\neasy for a person thoroughly imbued with the spirit of Inductive\nscience, though an atheist, to believe in a miracle\nwhich formed a part of a vast system, than for such a person,\nas a theist, to accept an isolated miracle.\n\n27. It is therefore with great prudence that Hume,\nand others after him, have practically insisted on commencing\nwith a discussion of the credibility of the single miracle,\ntreating the question as though the Christian Revelation\ncould be adequately regarded as a succession of such events.\nAs well might one consider the living body to be represented\nby the aggregate of the limbs which compose it. What is to\nbe complained of in so many popular discussions on the subject\nis the entire absence of any recognition of the different\nground on which the attackers and defenders of miracles are\nso often really standing. Proofs and illustrations are produced\nin endless number, which involving, as they almost all\ndo in the mind of the disputants on one side at least, that\nvery principle of causation, the absence of which in the case\nin question they are intended to establish, they fail in the\nsingle essential point. To attempt to induce any one to disbelieve\nin the existence of physical causation, in a given\ninstance, by means of illustrations which to him seem only\nadditional examples of the principle in question, is like trying\nto make a dam, in order to stop the flow of a river, by\nshovelling in snow. Such illustrations are plentiful in times\nof controversy, but being in reality only modified forms of\nthat which they are applied to counteract, they change their\nshape at their first contact with the disbeliever's mind, and\nonly help to swell the flood which they were intended to\ncheck.\n\n\n1. Reasons were given in the last chapter against the propriety of\n  applying the rules of Probability with any strictness to such\n  examples as these. But although all approach to numerical accuracy\n  is unattainable, we do undoubtedly recognize in ordinary life a\n  distinction between the credibility of one witness and another; such\n  a rough practical distinction will be quite sufficient for the\n  purposes of this chapter. For convenience, and to illustrate the\n  theory, the examples are best stated in a numerical form, but it is\n  not intended thereby to imply that any such accuracy is really\n  attainable in practice.\n\n2. I must plead guilty to this charge myself, in the first edition of\n  this work. The result was to make the treatment of this part of the\n  subject obscure and imperfect, and in some respects erroneous.\n\n3. The generalized algebraical form of this result is as follows. Let\n  p be the _\u00e0 priori_ probability of an event, and x be the\n  credibility of the witness. Then, if he asserts that the event\n  happened, the probability that it really did happen is\n  px/(px + (1 - p)(1 - x)); whilst if he asserts that it did _not_\n  happen the probability that it did happen is\n  p(1 - x)/(p(1 - x) + (1 - p)x).\n\n  In illustration of some remarks to be presently made, the reader\n  will notice that on making either of these expressions = p, we\n  obtain in each case x = 1/2. That is, a witness whose veracity = 1/2\n  leaves the _\u00e0 priori_ probability of an event (of this kind)\n  unaffected.\n\n  If, on the other hand, we make these expressions equal to x and 1 - x\n  respectively, we obtain in each case p = 1/2. That is, when an event\n  (of this kind) is as likely to happen as not, the ordinary veracity\n  of the witness in respect of it remains unaffected.\n\n4. Todhunter's _History_, p. 400. _Philosophical Magazine_, July, 1864.\n\n5. \"When therefore these two kinds of experience are contrary, we have\n  nothing to do but subtract the one from the other, and embrace an\n  opinion, either on one side or the other, with that assurance which\n  arises from the remainder.\" (Essay on Miracles.)\n\n6. Considerations of this kind have indeed been introduced into the\n  mathematical treatment of the subject. The common algebraical\n  solution of the problem in \u00a75 (to begin with the simplest case) is\n  of course as follows. Let p be the antecedent probability of the\n  event, and t the measure of the truthfulness of the witness; then\n  the chance of his statement being true is pt/(pt + (1 - p)(1 - t)).\n  This supposes him to lie as much when the event does not happen as\n  when it does. But we may meet the cases supposed in the text by\n  assuming that t' is the measure of his veracity when the event does\n  not happen, so that the above formula becomes pt/(pt + (1 - p)(1 - t')).\n  Here t' and t measure respectively his trustworthiness in usual and\n  unusual events. As a formal solution this certainly meets the\n  objections stated above in \u00a7\u00a714 and 15. The determination however\n  of t' would demand, as I have remarked, continually renewed appeal\n  to experience. In any case the practical methods which would be\n  adopted, if any plans of the kind indicated above were resorted to,\n  seem to me to differ very much from that adopted by the\n  mathematicians, in their spirit and plan.\n\n7. Laplace, for instance (_Essai_, ed. 1825, p. 149), says that if we\n  saw 100 dies (known of course to be fair ones) all give the same\n  face, we should be bewildered at the time, and need confirmation\n  from others, but that, after due examination, no one would feel\n  obliged to postulate hallucination in the matter. But the chance of\n  this occurrence is represented by a fraction whose numerator is 1,\n  and denominator contains 77 figures, and is therefore utterly\n  inappreciable by the imagination. It must be admitted, though, that\n  there is something hypothetical about such an example, for we could\n  not really know that the dies were fair with a confidence even\n  distantly approaching such prodigious odds. In other words, it is\n  difficult here to keep apart those different aspects of the question\n  discussed in Chap. XIV. \u00a7\u00a728-33.\n\n8. In the first edition this was stated, as it now seems to me, in\n  decidedly too unqualified a manner. It must be remembered, however,\n  that (as was shown in \u00a77) this plan is really the best theoretical\n  one which can be adopted in certain cases.\n\n9. It is on this principle that the remarkable conclusion mentioned on\n  p. 405 is based. Suppose an event whose probability is p; and that,\n  of a number of witnesses of the same veracity (y), m assert that it\n  happened, and n deny this. Generalizing the arithmetical reasoning\n  given above we see that the chance of the event being asserted\n  varies as\n\n  py^{m} (1 - y)^{n} + (1 - p) y^{n} (1 - y)^{m};\n\n  (viz. as the chance that the event happens, and that m are right and\n  n are wrong; _plus_ the chance that it does not happen, and that n\n  are right and m are wrong). And the chance of its being rightly\n  asserted as py^{m} (1 - y)^{n}. Therefore the chance that when we\n  have an assertion before us it is a true one is\n\n               py^{m} (1 - y)^{n}\n  ----------------------------------------------\n  py^{m} (1 - y)^{n} + (1 - p) y^{n} (1 - y)^{m},\n\n  which is equal to\n\n               py^{m-n}\n  --------------------------------\n  py^{m-n} + (1 - p) (1 - y)^{m-n}.\n\n  But this last expression represents the probability of an assertion\n  which is unanimously supported by m - n such witnesses.\n\n10. The stress which Butler lays upon this notion of a scheme is, I\n  think, one great merit of his _Analogy_.\n\n\n\n\nCHAPTER XVIII.\n\n\n_THE NATURE AND USE OF AN AVERAGE, AND ON THE DIFFERENT KINDS OF\nAVERAGE._[1]\n\n1. There is much need of some good account, accessible to the ordinary\n  English reader, of the nature and properties of the principal kinds\n  of Mean. The common text-books of Algebra suggest that there are\n  only three such, viz. the arithmetical, the geometrical and the\n  harmonical:--thus including two with which the statistician has\n  little or nothing to do, and excluding two or more with which he\n  should have a great deal to do. The best three references I can give\n  the reader are the following. (1) The article _Moyenne_ in the\n  _Dictionnaire des Sciences M\u00e9dicales_, by Dr Bertillon. This is\n  written somewhat from the Quetelet point of view. (2) A paper by\n  Fechner in the _Abhandlungen d. Math. phys. Classe\n  d. K\u00f6n. S\u00e4chs. Gesellschaft d. Wiss_. 1878; pp. 1-76. This contains\n  a very interesting discussion, especially for the statistician, of a\n  number of different kinds of mean. His account of the median is\n  remarkably full and valuable. But little mathematical knowledge is\n  demanded. (3) A paper by Mr F. Y. Edgeworth in the\n  _Camb. Phil. Trans._ for 1885, entitled _Observations and\n  Statistics_. This demands some mathematical knowledge. Instead of\n  dealing, as such investigations generally do, with only one Law of\n  Error and with only one kind of mean, it covers a wide field of\n  investigation.\n\n\n1. We have had such frequent occasion to refer to\n_averages_, and to the kind of uniformity which they are apt\nto display in contrast with individual objects or events, that\nit will now be convenient to discuss somewhat more minutely\nwhat are the different kinds of available average, and what\nexactly are the functions they perform.\n\nThe first vague notion of an average, as we now understand\nit, seems to me to involve little more than that of a\nsomething _intermediate_ to a number of objects. The objects\nmust of course resemble each other in certain respects, otherwise\nwe should not think of classing them together; and\nthey must also differ in certain respects, otherwise we should\nnot distinguish between them. What the average does for\nus, under this primitive form, is to enable us conveniently to\nretain the group together as a whole. That is, it furnishes a\nsort of representative value of the quantitative aspect of the\nthings in question, which will serve for certain purposes to\ntake the place of any single member of the group.\n\nIt would seem then that the first dawn of the conception\nwhich science reduces to accuracy under the designation of\nan average or mean, and then proceeds to subdivide into\nvarious distinct species of means, presents itself as performing\nsome of the functions of a general name. For what\nis the main use of a general name? It is to reduce a plurality\nof objects to unity; to group a number of things\ntogether by reference to some qualities which they possess\nin common. The ordinary general name rests upon a considerable\nvariety of attributes, mostly of a qualitative\ncharacter, whereas the average, in so far as it serves the\nsame sort of purpose, rests rather upon a single quantitative\nattribute. It directs attention to a certain kind and degree\nof magnitude. When the grazier says of his sheep that 'one\nwith another they will fetch about 50 shillings,' or the\nfarmer buys a lot of poles which 'run to about 10 feet,' it is\ntrue that they are not strictly using the equivalent of either\na general or a collective name. But they are coming very\nnear to such use, in picking out a sort of type or specimen of\nthe magnitude to which attention is to be directed, and in\nclassing the whole group by its resemblance to this type.\nThe grazier is thinking of his sheep: not in a merely general\nsense, as sheep, and therefore under that name or conception,\nbut as sheep of a certain approximate money value.\nSome will be more, some less, but they are all near enough\nto the assigned value to be conveniently classed together as\nif by a name. Many of our rough quantitative designations\nseem to be of this kind, as when we speak of 'eight-day\nclocks' or 'twelve-stone men,' &c.; unless of course we intend\n(as we sometimes do in these cases) to assign a maximum\nor minimum value. It is not indeed easy to see how else we\ncould readily convey a merely general notion of the quantitative\naspect of things, except by selecting a type as above,\nor by assigning certain limits within which the things are\nsupposed to lie.\n\n2. So far there is not necessarily any idea introduced\nof comparison,--of comparison, that is, of one group with\nanother,--by aid of such an average. As soon as we begin\nto think of this we have to be more precise in saying what\nwe mean by an average. We can easily see that the number\nof possible kinds of average, in the sense of intermediate\nvalues, is very great; is, in fact, indefinitely great. Out of\nthe general conception of an intermediate value, obtained by\nsome treatment of the original magnitudes, we can elicit as\nmany subdivisions as we please, by various modes of treatment.\nThere are however only three or four which for our\npurposes need be taken into account.\n\n(1) In the first place there is the arithmetical average\nor mean. The rule for obtaining this is very simple: add\nall the magnitudes together, and divide the sum by their\nnumber. This is the only kind of average with which the\nunscientific mind is thoroughly familiar. But we must not\nlet this simplicity and familiarity blind us to the fact that\nthere are definite reasons for the employment of this average,\nand that it is therefore appropriate only in definite circumstances.\nThe reason why it affords a safe and accurate\nintermediate value for the actual divergent values, is that\nfor many of the ordinary purposes of life, such as purchase\nand sale, we come to exactly the same result, whether we\ntake account of those existent divergences, or suppose all\nthe objects equated to their average. What the grazier\nmust be understood to mean, if he wishes to be accurate, by\nsaying that the average price of his sheep is 50 shillings, is,\nthat so far as that flock is concerned (and so far as he is\nconcerned), it comes to exactly the same thing, whether they\nare each sold at different prices, or are all sold at the 'average'\nprice. Accordingly, when he compares his sales of one\nyear with those of another; when he says that last year the\nsheep averaged 48 shillings against the 50 of this year; the\nemployment of this representative or average value is a great\nsimplification, and is perfectly accurate for the purpose in\nquestion.\n\n3. (2) Now consider this case. A certain population is\nfound to have doubled itself in 100 years: can we talk of an\n'average' increase here of 1 per cent. annually? The circumstances\nare not quite the same as in the former case, but\nthe analogy is sufficiently close for our purpose. The answer\nis decidedly, No. If 100 articles of any kind are sold for \u00a3100,\nwe say that the average price is \u00a31. By this we mean that\nthe total amount is the same whether the entire lot are sold\nfor \u00a3100, or whether we split the lot up into individuals\nand sell each of these for \u00a31. The average price here is a\nconvenient fictitious substitute, which can be applied for\neach individual without altering the aggregate total. If\ntherefore the question be, Will a supposed increase of 1 p. c.\nin each of the 100 years be equivalent to a total increase to\ndouble the original amount? we are proposing a closely\nanalogous question. And the answer, as just remarked, must\nbe in the negative. An annual increase of 1 p. c. continued\nfor 100 years will more than double the total; it will multiply\nit by about 2.7. The true annual increment required is measured\nby sqrt[100]{2}; that is, the population may be said to have\nincreased 'on the average' 0.7 p. c. annually.\n\nWe are thus directed to the second kind of average discussed\nin the ordinary text-books of algebra, viz. the geometrical.\nWhen only two quantities are concerned, with a single\nintermediate value between them, the geometrical mean constituting\nthis last is best described as the mean proportional\nbetween the two former. Thus, since 3 : sqrt{15} :: sqrt{15} : 5,\nsqrt{15} is the geometrical mean between 3 and 5. When a\nnumber of geometrical means have to be interposed between\ntwo quantities, they are to be so chosen that every term in\nthe entire succession shall bear the same constant ratio to\nits predecessor. Thus, in the example in the last paragraph,\n99 intermediate steps were to be interposed between 1 and 2,\nwith the condition that the 100 ratios thus produced were to\nbe all equal.\n\nIt would seem therefore that wherever accurate quantitative\nresults are concerned, the selection of the appropriate\nkind of average must depend upon the answer to the question,\nWhat particular intermediate value may be safely\nsubstituted for the actual variety of values, so far as the\nprecise object in view is concerned? This is an aspect of\nthe subject which will have to be more fully considered in\nthe next chapter. But it may safely be laid down that for\npurposes of general comparison, where accurate numerical\nrelations are not required, almost any kind of intermediate\nvalue will answer our purpose, provided we adhere to the\nsame throughout. Thus, if we want to compare the statures\nof the inhabitants of different counties or districts in England,\nor of Englishmen generally with those of Frenchmen,\nor to ascertain whether the stature of some particular class\nor district is increasing or diminishing, it really does not\nseem to matter what sort of average we select provided, of\ncourse, that we adhere to the same throughout our investigations.\nA very large amount of the work performed by\naverages is of this merely comparative or non-quantitative\ndescription; or, at any rate, nothing more than this is really\nrequired. This being so, we should naturally resort to the\narithmetical average; partly because, having been long in\nthe field, it is universally understood and appealed to, and\npartly because it happens to be remarkably simple and easy\nto calculate.\n\n4. The arithmetical mean is for most ordinary purposes\nthe simplest and best. Indeed, when we are dealing\nwith a small number of somewhat artificially selected magnitudes,\nit is the only mean which any one would think of\nemploying. We should not, for instance, apply any other\nmethod to the results of a few dozen measurements of lengths\nor estimates of prices.\n\nWhen, however, we come to consider the results of a very\nlarge number of measurements of the kind which can be\ngrouped together into some sort of 'probability curve' we\nbegin to find that there is more than one alternative before\nus. Begin by recurring to the familiar curve represented\non p. 29; or, better still, to the initial form of it represented\nin the next chapter (p. 476). We see that there are three\ndifferent ways in which we may describe the vertex of the\ncurve. We may call it the position of the _maximum_ ordinate;\nor that of the _centre_ of the curve; or (as will be seen\nhereafter) the point to which the arithmetical average of\nall the different values of the variable magnitude directs us.\nThese three are all distinct ways of describing a position;\nbut when we are dealing with a symmetrical curve at all\nresembling the binomial or exponential form they all three\ncoincide in giving the same result: as they obviously do in\nthe case in question.\n\nAs soon, however, as we come to consider the case of\nasymmetrical, or lop-sided curves, the indications given by\nthese three methods will be as a rule quite distinct; and\ntherefore the two former of these deserve brief notice as\nrepresenting different kinds of means from the arithmetical\nor ordinary one. We shall see that there is something about\neach of them which recommends it to common sense as being\nin some way natural and appropriate.\n\n5. (3) The first of these selects from amongst the\nvarious different magnitudes that particular one which is\nmost frequently represented. It has not acquired any technical\ndesignation,[1] except in so far as it is referred to, by\nits graphical representation, as the \"maximum ordinate\"\nmethod. But I suspect that some appeal to such a mean\nor standard is really far from uncommon, and that if we\ncould draw out into clearness the conceptions latent in the\njudgments of the comparatively uncultivated, we should find\nthat there were various classes of cases in which this mean\nwas naturally employed. Suppose, for instance, that there\nwas a fishery in which the fish varied very much in size\nbut in which the commonest size was somewhat near the\nlargest or the smallest. If the men were in the habit of\nselling their fish by _weight_, it is probable that they would\nbefore long begin to acquire some kind of notion of what\nis meant by the arithmetical mean or average, and would\nperceive that this was the most appropriate test. But if the\nfish were sorted into sizes, and sold by numbers in each of\nthese sizes, I suspect that this appeal to a maximum ordinate\nwould begin to take the place of the other. That is,\nthe most numerous class would come to be selected as a\nsort of type by which to compare the same fishery at one\ntime and another, or one fishery with others. There is also,\nas we shall see in the next chapter, some scientific ground\nfor the preference of this kind of mean in peculiar cases;\nviz. where the quantities with which we deal are true\n'errors,' in the estimate of some magnitude, and where also\nit is of much more importance to be exactly right, or very\nnearly right, than to have merely a low average of error.\n\n6. (4) The remaining kind of mean is that which is\nnow coming to be called the \"median.\" It is one with\nwhich the writings of Mr Galton have done so much to\nfamiliarize statisticians, and is best described as follows.\nConceive all the objects in question to be marshalled in the\norder of their magnitude; or, what comes to the same thing,\nconceive them sorted into a number of equally numerous\nclasses; then the middle one of the row, or the middle one\nin the middle class, will be the _median_. I do not think\nthat this kind of mean is at all generally recognized at\npresent, but if Mr Galton's scheme of natural measurement\nby what he calls \"per-centiles\" should come to be generally\nadopted, such a test would become an important one.\nThere are some conspicuous advantages about this kind of\nmean. For one thing, in most statistical enquiries, it is\nfar the simplest to calculate; and, what is more, the process\nof determining it serves also to assign another important\nelement to be presently noticed, viz. the 'probable error.'\nThen again, as Fechner notes, whereas in the arithmetical\nmean a few exceptional and extreme values will often cause\nperplexity by their comparative preponderance, in the case\nof the median (where their number only and not their extreme\nmagnitude is taken into account) the importance of\nsuch disturbance is diminished.\n\n7. A simple illustration will serve to indicate how these\nthree kinds of mean coalesce into one when we are dealing\nwith symmetrical Laws of Error, but become quite distinct\nas soon as we come to consider those which are unsymmetrical.\n\n[Figure: Various definitions of the mean.]\n\nSuppose that, in measuring a magnitude along OBDC,\nwhere the extreme limits are OB and OC, the law of error\nis represented by the triangle BAC: the length OD will\nbe at once the arithmetical mean, the median, and the most\nfrequent length: its frequency being represented by the\nmaximum ordinate AD. But now suppose, on the other\nhand, that the extreme lengths are OD and OC, and that\nthe triangle ADC represents the law of error. The most\nfrequent length will be the same as before, OD, marked by\nthe maximum ordinate AD. But the mean value will now\nbe OX, where DX = 1/3 DC; and the median will be OY,\nwhere DY = (1 - 1/sqrt{2}) DC.\n\nAnother example, taken from natural phenomena, may\nbe found in the heights of the barometer as taken at the\nsame hour on successive days. So far as 4857 of these may\nbe regarded as furnishing a sufficiently stable basis of experience,\nit certainly seems that the resulting curve of frequency\nis asymmetrical. The mean height here was found\nto be 29.98: the median was 30.01: the most frequent\nheight was 30.05. The close approximation amongst these\nis an indication that the asymmetry is slight.[2]\n\n8. It must be clearly understood that the average, of\nwhatever kind it may be, from the mere fact of its being a\nsingle substitute for an actual plurality of observed values,\nmust let slip a considerable amount of information. In fact\nit is only introduced for economy. It may entail no loss\nwhen used for some one assigned purpose, as in our example\nabout the sheep; but for purposes in general it\ncannot possibly take the place of the original diversity, by\nyielding all the information which they contained. If all\nthis is to be retained we must resort to some other method.\nPractically we generally do one of two things: either (1) we\nput all the figures down in statistical tables, or (2) we appeal\nto a diagram. This last plan is convenient when the\ndata are very numerous, or when we wish to display or to\ndiscover the nature of the law of facility under which they\nrange.\n\nThe mere assignment of an average lets drop nearly all\nof this, confining itself to the indication of an intermediate\nvalue. It gives a \"middle point\" of some kind, but says\nnothing whatever as to how the original magnitudes were\ngrouped about this point. For instance, whether two magnitudes\nhad been respectively 25 and 27, or 15 and 37, they\nwould yield the same arithmetical average of 26.\n\n9. To break off at this stage would clearly be to leave\nthe problem in a very imperfect condition. We therefore\nnaturally seek for some simple test which shall indicate\nhow closely the separate results were grouped about their\naverage, so as to recover some part of the information which\nhad been let slip.\n\nIf any one were approaching this problem entirely anew,--that\nis, if he had no knowledge of the mathematical exigencies\nwhich attend the theory of \"Least Squares,\"--I apprehend\nthat there is but one way in which he would set\nabout the business. He would say, The average which we\nhave already obtained gave us a rough indication, by assigning\nan intermediate point amongst the original magnitudes.\nIf we want to supplement this by a rough indication\nas to how near together these magnitudes lie, the\nbest way will be to treat their departures from the mean\n(what are technically called the \"errors\") in precisely the\nsame way, viz. by assigning _their_ average. Suppose there\nare 13 men whose heights vary by equal differences from\n5 feet to 6 feet, we should say that their average height\nwas 66 inches, and their average departure from this average\nwas 3-3/13 inches.\n\nLooked at from this point of view we should then proceed\nto try how each of the above-named averages would\nanswer the purpose. Two of them,--viz. the arithmetical\nmean and the median,--will answer perfectly; and, as we\nshall immediately see, are frequently used for the purpose.\nSo too we could, if we pleased, employ the geometrical\nmean, though such employment would be tedious, owing\nto the difficulty of calculation. The 'maximum ordinate'\nclearly would not answer, since it would generally (v. the\ndiagram on p. 443) refer us back again to the average\nalready obtained, and therefore give no information.\n\nThe only point here about which any doubt could arise\nconcerns what is called in algebra the _sign_ of the errors.\nTwo equal and opposite errors, added algebraically, would\ncancel each other. But when, as here, we are regarding\nthe errors as substantive quantities, to be considered on\ntheir own account, we attend only to their real magnitude,\nand then these equal and opposite errors are to be put upon\nexactly the same footing.\n\n10. Of the various means already discussed, two, as\njust remarked, are in common use. One of these is familiarly\nknown, in astronomical and other calculations, as\nthe 'Mean Error,' and is so absolutely an application of the\nsame principle of the arithmetical mean to the errors, that\nhas been already applied to the original magnitudes, that it\nneeds no further explanation. Thus in the example in the\nlast section the mean of the heights was 66 inches, the\nmean of the errors was 3-3/13 inches.\n\nThe other is the Median, though here it is always known\nunder another name, i.e. as the 'Probable Error';--a technical\nand decidedly misleading term. It is briefly defined\nas that error which we are as likely to exceed as to fall\nshort of: otherwise phrased, if we were to arrange all the\nerrors in the order of their magnitude, it corresponds to that\none of them which just bisects the row. It is therefore the\n'median' error: or, if we arrange all the magnitudes in successive\norder, and divide them into four equally numerous\nclasses,--what Mr Galton calls 'quartiles,'--the first and\nthird of the consequent divisions will mark the limits of\nthe 'probable error' on each side, whilst the middle one will\nmark the 'median.' This median, as was remarked, coincides,\nin symmetrical curves, with the arithmetical mean.\n\nIt is best to stand by accepted nomenclature, but the\nreader must understand that such an error is not in any\nstrict sense 'probable.' It is indeed highly improbable that\nin any particular instance we should happen to get just this\nerror: in fact, if we chose to be precise and to regard it as\none exact magnitude out of an infinite number, it would be\ninfinitely unlikely that we should hit upon it. Nor can it be\nsaid to be probable that we shall be _within_ this limit of the\ntruth, for, by definition, we are just as likely to exceed as to\nfall short. As already remarked (see note on p. 441), the\n'maximum ordinate' would have the best right to be regarded\nas indicating the really most probable value.\n\n11. (5) _The error of mean square._ As previously suggested, the plan\nwhich would naturally be adopted by any one who had no concern with\nthe higher mathematics of the subject, would be to take the 'mean\nerror' for the purpose of the indication in view. But a very different\nkind of average is generally adopted in practice to serve as a test of\nthe amount of divergence or dispersion. Suppose that we have the\nmagnitudes x_{1}, x_{2}, ... x_{n}; their ordinary average is\n1/n (x_{1} + x_{2} + ... + x_{n}), and their 'errors' are the\ndifferences between this and x_{1}, x_{2}, ... x_{n}. Call these errors\ne_{1}, e_{2}, ... e_{n}, then the arithmetical mean of these errors\n(irrespective of sign) is 1/n (e_{1} + e_{2} + ... + e_{n}). The Error\nof Mean Square,[3] on the other hand, is the square root of\n1/n (e_{1}^{2} + e_{2}^{2} + ... + e_{n}^{2}).\n\nThe reasons for employing this latter kind of average in\npreference to any of the others will be indicated in the following\nchapter. At present we are concerned only with the\ngeneral logical nature of an average, and it is therefore\nsufficient to point out that any such intermediate value will\nanswer the purpose of giving a rough and summary indication\nof the degree of closeness of approximation which our\nvarious measures display to each other and to their common\naverage. If we were to speak respectively of the 'first' and\nthe 'second average,' we might say that the former of these\nassigns a rough single substitute for the plurality of original\nvalues, whilst the latter gives a similar rough estimate of the\ndegree of their departure from the former.\n\n12. So far we have only been considering the general\nnature of an average, and the principal kinds of average\npractically in use. We must now enquire more particularly\nwhat are the principal purposes for which averages are employed.\n\nIn this respect the first thing we have to do is to raise\ndoubts in the reader's mind on a subject on which he\nperhaps has not hitherto felt the slightest doubt. Every\none is more or less familiar with the practice of appealing to\nan average in order to secure accuracy. But distinctly what\nwe begin by doing is to sacrifice accuracy; for in place of\nthe plurality of actual results we get a single result which\nvery possibly does not agree with any one of them. If I find\nthe temperature in different parts of a room to be different,\nbut say that the average temperature is 61\u00b0, there may perhaps\nbe but few parts of the room where this exact temperature\nis realized. And if I say that the average stature of\na certain small group of men is 68 inches, it is probable that\nno one of them will present precisely this height.\n\nThe principal way in which accuracy can be thus secured\nis when what we are really aiming at is not the magnitudes\nbefore us but something else of which they are an indication.\nIf they are themselves 'inaccurate,'--we shall see presently\nthat this needs some explanation,--then the single average,\nwhich in itself agrees perhaps with none of them, may be\nmuch more nearly what we are actually in want of. We shall\nfind it convenient to subdivide this view of the subject into\ntwo parts; by considering first those cases in which quantitative\nconsiderations enter but slightly, and in which no determination\nof the particular Law of Error involved is demanded,\nand secondly those in which such determination cannot be\navoided. The latter are only noticed in passing here, as a\nseparate chapter is reserved for their fuller consideration.\n\n13. The process, as a practical one, is familiar enough\nto almost everybody who has to work with measures of any\nkind. Suppose, for instance, that I am measuring any object\nwith a brass rod which, as we know, expands and contracts\naccording to the temperature. The results will vary slightly,\nbeing sometimes a little too great and sometimes a little too\nsmall. All these variations are physical facts, and if what\nwe were concerned with was the properties of brass they\nwould be the one important fact for us. But when we are\nconcerned with the length of the object measured, these facts\nbecome superfluous and misleading. What we want to do is\nto escape their influence, and this we are enabled to effect by\ntaking their (arithmetical) average, provided only they are\nas often in excess as in defect.[4] For this purpose all that is\nnecessary is that equal excesses and defects should be\nequally prevalent. It is not necessary to know what is the\nlaw of variation, or even to be assured that it is of one particular\nkind. Provided only that it is in the language of\nthe diagram on p. 29, symmetrical, then the arithmetical\naverage of a suitable and suitably varied number of measurements\nwill be free from this source of disturbance. And\nwhat holds good of this cause of variation will hold good of\nall others which obey the same general conditions. In fact\nthe equal prevalence of equal and opposite errors seems to\nbe the sole and sufficient justification of the familiar process\nof taking the average in order to secure accuracy.\n\n14. We must now make the distinction to which attention\nrequires so often to be drawn in these subjects\nbetween the cases in which there respectively is, and is not,\nsome objective magnitude aimed at: a distinction which the\ncommon use of the same word \"errors\" is so apt to obscure.\nWhen we talked, in the case of the brass rod, of excesses\nand defects being equal, we meant exactly what we said, viz.\nthat for every case in which the 'true' length (i.e. that determined\nby the authorized standard) is exceeded by a given\nfraction of an inch, there will be a corresponding case in\nwhich there is an equal defect.\n\nOn the other hand, when there is no such fixed objective\nstandard of reference, it would appear that all that we mean\nby equal excesses and defects is permanent symmetry of\narrangement. In the case of the measuring rod we were\nable to start with something which existed, so to say, before\nits variations; but in many cases any starting point which\nwe can find is solely determined by the average.\n\nSuppose, for instance, we take a great number of observations\nof the height of the barometer at a certain place,\nat all times and seasons and in all weathers, we should\ngenerally consider that the average of all these showed the\n'true' height for that place. What we really mean is that\nthe height at any moment is determined partly (and principally)\nby the height of the column of air above it, but partly\nalso by a number of other agencies such as local temperature,\nmoisture, wind, &c. These are sometimes more and sometimes\nless effective, but their range being tolerably constant,\nand their distribution through this range being\ntolerably symmetrical, the average of one large batch of\nobservations will be almost exactly the same as that of any\nother. This constancy of the average _is_ its truth. I am\nquite aware that we find it difficult not to suppose that\nthere must be something more than this constancy, but we\nare probably apt to be misled by the analogy of the other\nclass of cases, viz. those in which we are really aiming at\nsome sort of mark.\n\n15. As regards the practical methods available for\ndetermining the various kinds of average there is very little\nto be said; as the arithmetical rules are simple and definite,\nand involve nothing more than the inevitable drudgery\nattendant upon dealing with long rows of figures. Perhaps\nthe most important contribution to this part of the subject is\nfurnished by Mr Galton's suggestion to substitute the median\nfor the mean, and thus to elicit the average with sufficient\naccuracy by the mere act of grouping a number of objects\ntogether. Thus he has given an ingenious suggestion for\nobtaining the average height of a number of men without\nthe trouble and risk of measuring them all. \"A barbarian\nchief might often be induced to marshall his men in the\norder of their heights, or in that of the popular estimate of\ntheir skill in any capacity; but it would require some apparatus\nand a great deal of time to measure each man\nseparately, even supposing it possible to overcome the usually\nstrong repugnance of uncivilized people to any such proceeding\"\n(_Phil. Mag._ Jan. 1875). That is, it being known\nfrom wide experience that the heights of any tolerably\nhomogeneous set of men are apt to group themselves symmetrically,--the\ncondition for the coincidence of the three\nprincipal kinds of mean,--the middle man of a row thus\narranged in order will represent the mean or average man,\nand him we may subject to measurement. Moreover, since\nthe intermediate heights are much more thickly represented\nthan the extreme ones, a moderate error in the selection of\nthe central man of a long row will only entail a very small\nerror in the selection of the corresponding height.\n\n16. We can now conveniently recur to a subject which\nhas been already noticed in a former chapter, viz. the attempt\nwhich is sometimes made to establish a distinction\nbetween an average and a mean. It has been proposed to\nconfine the former term to the cases in which we are dealing\nwith a fictitious result of our own construction, that is, with\na mere arithmetical deduction from the observed magnitudes,\nand to apply the latter to cases in which there is\nsupposed to be some objective magnitude peculiarly representative\nof the average.\n\nRecur to the three principal classes, of things appropriate\nto Probability, which were sketched out in Ch. II. \u00a74. The\nfirst of these comprised the results of games of chance. Toss\na die ten times: the total number of pips on the upper\nside may vary from ten up to sixty. Suppose it to be\nthirty. We then say that the average of this batch of\nten is three. Take another set of ten throws, and we may\nget another average, say four. There is clearly nothing\nobjective peculiarly corresponding in any way to these\naverages. No doubt if we go on long enough we shall\nfind that the averages tend to centre about 3.5: we then\ncall this _the_ average, or the 'probable' number of points;\nand this ultimate average might have been pretty constantly\nasserted beforehand from our knowledge of the constitution\nof a die. It has however no other truth or reality\nabout it of the nature of a type: it is simply the limit\ntowards which the averages tend.\n\nThe next class is that occupied by the members of most\nnatural groups of objects, especially as regards the characteristics\nof natural species. Somewhat similar remarks may\nbe repeated here. There is very frequently a 'limit' towards\nwhich the averages of increasing numbers of individuals tend\nto approach; and there is certainly some temptation to regard\nthis limit as being a sort of type which all had been\nintended to resemble as closely as possible. But when we\nlooked closer, we found that this view could scarcely be\njustified; all which could be safely asserted was that this\ntype represented, for the time being, the most numerous\nspecimens, or those which under existing conditions could\nmost easily be produced.\n\nThe remaining class stands on a somewhat different\nground. When we make a succession of more or less successful\nattempts of any kind, we get a corresponding series\nof deviations from the mark at which we aimed. These we\nmay treat arithmetically, and obtain their averages, just as\nin the former cases. These averages are fictions, that is to\nsay, they are artificial deductions of our own which need\nnot necessarily have anything objective corresponding to\nthem. In fact, if they be averages of a _few_ only they\nmost probably will not have anything thus corresponding\nto them. Anything answering to a type can only be sought\nin the 'limit' towards which they ultimately tend, for this\nlimit coincides with the fixed point or object aimed at.\n\n17. Fully admitting the great value and interest of\nQuetelet's work in this direction,--he was certainly the first\nto direct public attention to the fact that so many classes of\nnatural objects display the same characteristic property,--it\nnevertheless does not seem desirable to attempt to mark\nsuch a distinction by any special use of these technical\nterms. The objections are principally the two following.\n\nIn the first place, a single antithesis, like this between\nan average and a mean, appears to suggest a very much\nsimpler state of things than is actually found to exist in\nnature. A reference to the three classes of things just\nmentioned, and a consideration of the wide range and diversity\nincluded in each of them, will serve to remind us\nnot only of the very gradual and insensible advance from\nwhat is thus regarded as 'fictitious' to what is claimed as\n'real;' but also of the important fact that whereas the 'real\ntype' may be of a fluctuating and evanescent character, the\n'fiction' may (as in games of chance) be apparently fixed\nfor ever. Provided only that the conditions of production\nremain stable, averages of large numbers will always practically\npresent much the same general characteristics. The\nfar more important distinction lies between the average of\na few, with its fluctuating values and very imperfect and\noccasional attainment of its ultimate goal, and the average\nof many and its gradually close approximation to its ultimate\nvalue: i.e. to its objective point of aim if there happen\nto be such.\n\nThen, again, the considerations adduced in this chapter\nwill show that within the field of the average itself there is\nfar more variety than Quetelet seems to have recognized.\nHe did not indeed quite ignore this variety, but he practically\nconfined himself almost entirely to those symmetrical\narrangements in which three of the principal means coalesce\ninto one. We should find it difficult to carry out his distinction\nin less simple cases. For instance, when there is\nsome degree of asymmetry, it is the 'maximum ordinate'\nwhich would have to be considered as a 'mean' to the\nexclusion of the others; for no appeal to an arithmetical\naverage would guide us to this point, which however is to\nbe regarded, if any can be so regarded, as marking out the\nposition of the ultimate type.\n\n18. We have several times pointed out that it is a\ncharacteristic of the things with which Probability is concerned\nto present, in the long run, a continually intensifying\nuniformity. And this has been frequently described as what\nhappens 'on the average.' Now an objection may very\npossibly be raised against regarding an arrangement of\nthings by virtue of which order thus emerges out of disorder\nas deserving any special notice, on the ground that from the\nnature of the arithmetical average it could not possibly be\notherwise. The process by which an average is obtained, it\nmay be urged, insures this tendency to equalization amongst\nthe magnitudes with which it deals. For instance, let there\nbe a party of ten men, of whom four are tall and four are\nshort, and take the average of any five of them. Since this\nnumber cannot be made up of tall men only, or of short men\nonly, it stands to reason that the averages cannot differ so\nmuch amongst themselves as the single measures can. Is\nnot then the equalizing process, it may be asked, which is\nobservable on increasing the range of our observations,\none which can be shown to follow from necessary laws of\narithmetic, and one therefore which might be asserted _\u00e0 priori_?\n\nWhatever force there may be in the above objection arises\nprincipally from the limitations of the example selected, in\nwhich the number chosen was so large a proportion of the\ntotal as to exclude the bare possibility of only extreme cases\nbeing contained within it. As much confusion is often felt\nhere between what is necessary and what is matter of experience,\nit will be well to look at an example somewhat\nmore closely, in order to determine exactly what are the\nreally necessary consequences of the averaging process.\n\n19. Suppose then that we take ten digits at random\nfrom a table (say) of logarithms. Unless in the highly unlikely\ncase of our having happened upon the same digit ten\ntimes running, the average of the ten _must_ be intermediate\nbetween the possible extremes. Every conception of an\naverage of any sort not merely involves, but actually means,\nthe taking of something intermediate between the extremes.\nThe average therefore of the ten must lie closer to 4.5 (the\naverage of the extremes) than did some of the single digits.\n\nNow suppose we take 1000 such digits instead of 10. We\ncan say nothing more about the larger number, with demonstrative\ncertainty, than we could before about the smaller.\nIf they were unequal to begin with (i.e. if they were not all\nthe same) then the average _must_ be intermediate, but more\nthan this cannot be proved arithmetically. By comparison with\nsuch purely arithmetical considerations there is what may be\ncalled a physical fact underlying our confidence in the growing\nstability of the average of the larger number. It is that\nthe constituent elements from which the average is deduced\nwill themselves betray a growing uniformity:--that the proportions\nin which the different digits come out will become\nmore and more nearly equal as we take larger numbers of\nthem. If the proportions in which the 1000 digits were\ndistributed were the same as those of the 10 the averages\nwould be the same. It is obvious therefore that the arithmetical\nprocess of obtaining an average goes a very little\nway towards securing the striking kind of uniformity which\nwe find to be actually presented.\n\n20. There is another way in which the same thing\nmay be put. It is sometimes said that whatever may have\nbeen the arrangement of the original elements the process of\ncontinual averaging will necessarily produce the peculiar\nbinomial or exponential law of arrangement. This statement\nis perfectly true (with certain safeguards) but it is not\nin any way opposed to what has been said above. Let us\ntake for consideration the example above referred to. The\narrangement of the individual digits in the long run is the\nsimplest possible. It would be represented, in a diagram,\nnot by a curve but by a finite straight line, for each digit\noccurs about as often as any other, and this exhausts all the\n'arrangement' that can be detected. Now, when we consider\nthe results of taking averages of ten such digits, we see\nat once that there is an opening for a more extensive arrangement.\nThe totals may range from 0 up to 100, and therefore\nthe average will have 100 values from 0 to 9; and what\nwe find is that the frequency of these numbers is determined\naccording to the Binomial[5] or Exponential Law. The most\nfrequent result is the true mean, viz. 4.5, and from this they\ndiminish in each direction towards 0 and 10, which will each\noccur but once (on the average) in 10^{10} occasions.\n\nThe explanation here is of the same kind as in the former\ncase. The resultant arrangement, so far as the averages are\nconcerned, is only 'necessary' in the sense that it is a necessary\nresult of certain physical assumptions or experiences.\nIf all the digits tend to occur with equal frequency, and if\nthey are 'independent' (i.e. if each is associated indifferently\nwith every other), then it is an arithmetical consequence\nthat the averages when arranged in respect of their magnitude\nand prevalence will display the Law of Facility above\nindicated. Experience, so far as it can be appealed to, shows\nthat the true randomness of the selection of the digits,--i.e.\ntheir equally frequent recurrence, and the impartiality of\ntheir combination,--is very fairly secured in practice. Accordingly\nthe theoretic deduction that whatever may have\nbeen the original Law of Facility of the individual results\nwe shall always find the familiar Exponential Law asserting\nitself as the law of the averages, is fairly justified by experience\nin such a case.\n\nThe further discussion of certain corrections and refinements\nis reserved to the following chapter.\n\n21. In regard to the three kinds of average employed\nto test the amount of dispersion,--i.e. the mean error, the\nprobable error, and the error of mean square,--two important\nconsiderations must be borne in mind. They will\nboth recur for fuller discussion and justification in the course\nof the next chapter, when we come to touch upon the Method\nof Least Squares, but their significance for logical purposes\nis so great that they ought not to be entirely passed by at\npresent.\n\n(1) In the first place, then, it must be remarked that in\norder to know what in any case is the real value of an error\nwe ought in strictness to know what is the position of the\nlimit or ultimate average, for the amount of an error is\nalways theoretically measured from this point. But this is\ninformation which we do not always possess. Recurring\nonce more to the three principal classes of events with which\nwe are concerned, we can readily see that in the case of\ngames of chance we mostly do possess this knowledge. Instead\nof appealing to experience to ascertain the limit, we\npractically deduce it by simple mechanical or arithmetical\nconsiderations, and then the 'error' in any individual case or\ngroup of cases is obviously found by comparing the results\nthus obtained with that which theory informs us would ultimately\nbe obtained in the long run. In the case of deliberate\nefforts at an aim (the third class) we may or may\nnot know accurately the value or position of this aim. In\nastronomical observations we do not know it, and the method\nof Least Squares is a method for helping us to ascertain it as\nwell as we can; in such experimental results as firing at a\nmark we do know it, and may thus test the nature and\namount of our failure by direct experience. In the remaining\ncase, namely that of what we have termed natural kinds\nor groups of things, not only do we not know the ultimate\nlimit, but its existence is always at least doubtful, and in\nmany cases may be confidently denied. Where it does exist,\nthat is, where the type seems for all practical purposes permanently\nfixed, we can only ascertain it by a laborious resort\nto statistics. Having done this, we may then test by it the\nresults of observations on a small scale. For instance, if we\nfind that the ultimate proportion of male to female births is\nabout 106 to 100, we may then compare the statistics of\nsome particular district or town and speak of the consequent\n'error,' viz. the departure, in that particular and special\ndistrict, from the general average.\n\nWhat we have therefore to do in the vast majority of\npractical cases is to take the average of a finite number of\nmeasurements or observations,--of all those, in fact, which\nwe have in hand,--and take _this_ as our starting point in\norder to measure the errors. The errors in fact are not\nknown for certain but only probably calculated. This however\nis not so much of a theoretic defect as it may seem at\nfirst sight; for inasmuch as we seldom have to employ these\nmethods,--for purposes of calculation, that is, as distinguished\nfrom mere illustration,--except for the purpose of discovering\nwhat the ultimate average is, it would be a sort of\n_petitio principii_ to assume that we had already secured it.\nBut it is worth while considering whether it is desirable to\nemploy one and the same term for 'errors' known to be\nsuch, and whose amount can be assigned with certainty, and\nfor 'errors' which are only probably such and whose amount\ncan be only probably assigned. In fact it has been proposed[6]\nto employ the two terms 'error' and 'residual' respectively\nto distinguish between the magnitudes thus determined, that\nis, between the (generally unknown) actual error and the observed\nerror.\n\n22. (2) The other point involves the question to what\nextent either of the first two tests (pp. 446,7) of the closeness\nwith which the various results have grouped themselves\nabout their average is trustworthy or complete. The answer\nis that they are necessarily incomplete. No single estimate\nor magnitude can possibly give us an adequate account of a\nnumber of various magnitudes. The point is a very important\none; and is not, I think, sufficiently attended to, the\nconsequence being, as we shall see hereafter, that it is far\ntoo summarily assumed that a method which yields the\nresult with the least 'error of mean square' must necessarily\nbe the best result for all purposes. It is not however by any\nmeans clear that a test which answers best for one purpose\nmust do so for all.\n\nIt must be clearly understood that each of these tests is\nan 'average,' and that every average necessarily rejects a\nmass of varied detail by substituting for it a single result.\nWe had, say, a lot of statures: so many of 60 inches, so\nmany of 61, &c. We replace these by an 'average' of 68,\nand thereby drop a mass of information. A portion of this\nwe then seek to recover by reconsidering the 'errors' or\ndepartures of these statures from their average. As before,\nhowever, instead of giving the full details we substitute an\naverage of the errors. The only difference is that instead of\ntaking the same kind of average (i.e. the arithmetical) we\noften prefer to adopt the one called the 'error of mean\nsquare.'\n\n23. A question may be raised here which is of sufficient\nimportance to deserve a short consideration. When we have\ngot a set of measurements before us, why is it generally\nheld to be sufficient simply to assign: (1) the mean value;\nand (2) the mean departure from this mean? The answer\nis, of course, partly given by the fact that we are only supposed\nto be in want of a rough approximation: but there is\nmore to be said than this. A further justification is to be\nfound in the fact that we assume that we need only contemplate\nthe possibility of a single Law of Error, or at any\nrate that the departures from the familiar Law will be but\ntrifling. In other words, if we recur to the figure on p. 29,\nwe assume that there are only two unknown quantities or\ndisposable constants to be assigned; viz. first, the position of\nthe centre, and, secondly, the degree of eccentricity, if one\nmay so term it, of the curve. The determination of the\nmean value directly and at once assigns the former, and the\ndetermination of the mean error (in either of the ways referred\nto already) indirectly assigns the latter by confining us\nto one alone of the possible curves indicated in the figure.\n\nExcept for the assumption of one such Law of Error the\ndetermination of the mean error would give but a slight\nintimation of the sort of outline of our Curve of Facility.\nWe might then have found it convenient to adopt some plan\nof successive approximation, by adding a third or fourth\n'mean.' Just as we assign the mean value of the magnitude,\nand its mean departure from this mean; so we might\ntake this mean error (however determined) as a fresh starting\npoint, and assign the mean departure from it. If the point\nwere worth further discussion we might easily illustrate by\nmeans of a diagram the sort of successive approximations\nwhich such indications would yield as to the ultimate form\nof the Curve of Facility or Law of Error.\n\n*        *        *        *        *\n\nAs this volume is written mainly for those who take an interest in the\nlogical questions involved, rather than as an introduction to the actual\nprocesses of calculation, mathematical details have been throughout avoided\nas much as possible. For this reason comparatively few references have\nbeen made to the exponential equation of the Law of Error, or to the\ncorresponding 'Probability integral,' tables of which are given in several\nhandbooks on the subject. There are two points however in connection\nwith these particular topics as to which difficulties are, or should be,\nfelt by so many students that some notice may be taken of them here\n\n(1) In regard to the ordinary algebraical expression for the law of\nerror, viz. y = (h/sqrt{\u03c0}) e^{-h^{2}x^{2}}, it will have been\nobserved that I have always spoken of y as being _proportional_ to the\nnumber of errors of the particular magnitude x. It would hardly be\ncorrect to say, absolutely, that y _represents_ that number, because\nof course the actual number of errors of any precise magnitude, where\ncontinuity of possibility is assumed, must be indefinitely small. If\ntherefore we want to pass from the continuous to the discrete, by\nascertaining the actual number of errors between two consecutive\ndivisions of our scale, when, as usual in measurements, all within\ncertain limits are referred to some one precise point, we must modify\nour formula. In accordance with the usual differential notation, we\nmust say that the number of errors falling into one subdivision (dx)\nof our scale _is_ dx (h/sqrt{\u03c0}) e^{-h^{2} x^{2}}, where dx is a\n(small) unit of length, in which both h^{-1} and x must be measured.\n\nThe difficulty felt by most students is in applying the formula to\nactual statistics, in other words in putting in the correct units. To\ntake an actual numerical example, suppose that 1460 men have been\nmeasured in regard to their height \"true to the nearest inch,\" and let\nit be known that the modulus here is 3.6 inches. Then dx = 1 (inch);\nh^{-1} = 3.6 inches. Now sum (h/sqrt{\u03c0}) e^{-h^{2}x^{2}} dx = 1; that\nis, the sum of all the consecutive possible values is equal to\n_unity_. When therefore we want the sum, as here, to be 1460, we must\nexpress the formula thus;--y = 1460/(sqrt{\u03c0} \u00d7 3.6) e^{-(x/3.6)^{2}},\nor y = 228 e^{-(x/3.6)^{2}}.\n\nHere x stands for the number of inches measured from the central or\nmean height, and y stands for the number of men referred to that\nheight in our statistical table. (The values of e^{-t^{2}} for\nsuccessive values of t are given in the handbooks.)\n\nFor illustration I give the calculated numbers by this formula for values\nof x from 0 to 8 inches, with the actual numbers observed in the Cambridge\nmeasurements recently set on foot by Mr Galton.\n\ninches  calculated observed\nx = 0     y = 228    = 231\nx = 1     y = 212    = 218\nx = 2     y = 166    = 170\nx = 3     y = 111    = 110\nx = 4     y =  82    =  66\nx = 5     y =  32    =  31\nx = 6     y =  11    =  10\nx = 7     y =   4    =   6\nx = 8     y =   1    =   3\n\nHere the average height was 69 inches: dx, as stated, = 1 inch. By\nsaying, 'put x = 0,' we mean, calculate the number of men who are assigned\nto 69 inches; i.e. who fall between 68.5 and 69.5. By saying, 'put x = 4,'\nwe mean, calculate the number who are assigned to 65 or to 73; i.e. who lie\nbetween 64.5 and 65.5, or between 72.5 and 73.5. The observed results, it\nwill be seen, keep pretty close to the calculated: in the case of the former\nthe _means_ of equal and opposite divergences from the mean have been taken,\nthe actual results not being always the same in opposite directions.\n\n(2) The other point concerns the interpretation of the familiar\nprobability integral, (2/sqrt{\u03c0}) integral_{0}^{t} e^{-t^{2}} dt.\nEvery one who has calculated the chance of an event, by the help\nof the tables of this integral given in so many handbooks, knows that\nif we assign any numerical value to t, the corresponding value of the\nabove expression assigns the chance that an error taken at random\nshall lie within that same limit, viz. t. Thus put t = 1.5, and we\nhave the result 0.96; that is, only 4 per cent. of the errors will\nexceed 'one and a half.' But when we ask, 'one and a half' _what?_ the\nanswer would not always be very ready. As usual, the main difficulty\nof the beginner is not to manipulate the formul\u00e6, but to be quite\nclear about his units.\n\nIt will be seen at once that this case differs from the preceding in that\nwe cannot now choose our unit as we please. Where, as here, there is only\none variable (t), if we were allowed to select our own unit, the inch, foot,\nor whatever it might be, we might get quite different results. Accordingly\nsome comparatively natural unit must have been chosen for us in which we\nare bound to reckon, just as in the circular measurement of an angle as\ndistinguished from that by degrees.\n\nThe answer is that the unit here is the _modulus_, and that to put 't = 1.5'\nis to say, 'suppose the error half as great again as the modulus'; the\nmodulus itself being an error of a certain assignable magnitude depending\nupon the nature of the measurements or observations in question. We shall\nsee this better if we put the integral in the form\n(2/sqrt{\u03c0}) integral_{0}^{hx} e^{-h^{2} x^{2}} d(hx);\nwhich is precisely equivalent, since the value of a definite integral is\nindependent of the particular variable employed. Here hx is the same as\nx : 1/h; i.e. it is the ratio of x to 1/h, or x measured in terms of 1/h.\nBut 1/h is the modulus in the equation\n(y = (h/sqrt{\u03c0}) e^{-h^{2} x^{2}})\nfor the law of error. In other words the numerical value of an error in\nthis formula, is the number of times, whole or fractional, which it\ncontains the modulus.\n\n\n1. This kind of mean is called by Fechner and others the \"_dichteste\n  Werth_.\" The most appropriate appeal to it that I have seen is by\n  Prof. Lexis (_Massenerscheinungen_, p. 42) where he shows that it\n  indicates clearly a sort of normal length of human life, of about 70\n  years; a result which is almost entirely masked when we appeal to\n  the arithmetical average.\n\n  This mean _ought_ to be called the 'probable' value (a name however\n  in possession of another) on the ground that it indicates the point\n  of likeliest occurrence; i.e. if we compare all the indefinitely\n  small and equal units of variation, the one corresponding to this\n  will tend to be most frequently represented.\n\n2. A diagram illustrative of this number of results was given in\n  _Nature_ (Sept. 1, 1887). In calculating, as above, the different\n  means, I may remark that the original results were given to three\n  decimal places; but, in classing them, only one place was\n  noted. That is, 29.9 includes all values between 29.900 and 29.999.\n  Thus the value most frequently entered in my tables was 30.0, but on\n  the usual principles of interpolation this is reckoned as 30.05.\n\n3. There is some ambiguity in the phraseology in use here. Thus Airy\n  commonly uses the expression 'Error of Mean Square' to represent, as\n  here, sqrt{(sum e^{2})/n}. Galloway commonly speaks of the 'Mean\n  Square of the Errors' to represent (sum e^{2})/n. I shall adhere to\n  the former usage and represent it briefly by E.M.S. Still more\n  unfortunate (to my thinking) is the employment, by Mr Merriman and\n  others, of the expression 'Mean Error,' (widely in use in its more\n  natural signification,) as the equivalent of this E.M.S.\n\n  The technical term 'Fluctuation' is applied by Mr F. Y. Edgeworth to\n  the expression (2 sum e^{2})/n.\n\n4. Practically, of course, we should allow for the expansion or\n  contraction. But for purposes of logical explanation we may\n  conveniently take this variation as a specimen of one of those\n  disturbances which may be neutralised by resort to an average.\n\n5. More strictly _multinomial_: the relative frequency of the\n  different numbers being indicated by the coefficients of the powers\n  of x in the development of\n\n  (1 + x + x^{2} + ... + x^{9})^{10}.\n\n6. By Mr Merriman, in his work on _Least Squares_.\n\n\n\n\nCHAPTER XIX.\n\n\n_THE THEORY OF THE AVERAGE AS A MEANS OF APPROXIMATION TO THE TRUTH._\n\n1. In the last chapter we were occupied with the Average\nmainly under its qualitative rather than its quantitative\naspect. That is, we discussed its general nature, its principal\nvarieties, and the main uses to which it could be put in\nordinary life or in reasoning processes which did not claim to\nbe very exact. It is now time to enter more minutely into\nthe specific question of the employment of the average in\nthe way peculiarly appropriate to Probability. That is, we\nmust be supposed to have a certain number of measurements,--in\nthe widest sense of that term,--placed before us,\nand to be prepared to answer such questions as; Why do we\ntake their average? With what degree of confidence?\nMust we in all cases take the average, and, if so, one always\nof the same kind?\n\nThe subject upon which we are thus entering is one\nwhich, under its most general theoretic treatment, has perhaps\ngiven rise to more profound investigation, to a greater\nvariety of opinion, and in consequence to a more extensive\nhistory and literature, than any other single problem within\nthe range of mathematics.[1] But, in spite of this, the main\nlogical principles underlying the methods and processes in\nquestion are not, I apprehend, particularly difficult to grasp:\nthough, owing to the extremely technical style of treatment\nadopted even in comparatively elementary discussions of the\nsubject, it is far from easy for those who have but a moderate\ncommand of mathematical resources to disentangle these\nprinciples from the symbols in which they are clothed. The\npresent chapter contains an attempt to remove these difficulties,\nso far as a general comprehension of the subject is concerned.\nAs the treatment thus adopted involves a considerable\nnumber of subdivisions, the reader will probably\nfind it convenient to refer back occasionally to the table of\ncontents at the commencement of this volume.\n\n2. The subject, in the form in which we shall discuss\nit, will be narrowed to the consideration of the _average_, on\naccount of the comparative simplicity and very wide prevalence\nof this aspect of the problem. The problem is however\nvery commonly referred to, even in non-mathematical treatises,\nas the Rule or Method of Least Squares; the fact being\nthat, in such cases as we shall be concerned with, the Rule\nof Least Squares resolves itself into the simpler and more\nfamiliar process of taking the arithmetical average. A very\nsimple example,--one given by Herschel,--will explain the\ngeneral nature of the task under a slightly wider treatment,\nand will serve to justify the familiar designation.\n\nSuppose that a man had been firing for some time with a\npistol at a small mark, say a wafer on a wall. We may take\nit for granted that the shot-marks would tend to group\nthemselves about the wafer as a centre, with a density varying\nin some way inversely with the distance from the centre.\nBut now suppose that the wafer which marked the centre\nwas removed, so that we could see nothing but the surface of\nthe wall spotted with the shot-marks; and that we were\nasked to guess the position of the wafer. Had there been\nonly _one_ shot, common sense would suggest our assuming\n(of course very precariously) that this marked the real centre.\nHad there been two, common sense would suggest our taking\nthe mid-point between them. But if three or more were\ninvolved, common sense would be at a loss. It would feel\nthat some intermediate point ought to be selected, but\nwould not see its way to a more precise determination, because\nits familiar reliance,--the arithmetical average,--does\nnot seem at hand here. The rule in question tells us how to\nproceed. It directs us to select that point which will render\nthe sum of the squares of all the distances of the various\nshot-marks from it the least possible.[2]\n\nThis is merely by way of illustration, and to justify the\nfamiliar designation of the rule. The sort of cases with\nwhich we shall be exclusively occupied are those comparatively\nsimple ones in which only linear magnitude, or some\nquality which can be adequately represented by linear magnitude,\nis the object under consideration. In respect of these\nthe Rule of Least Squares reduces itself to the process of\ntaking the average, in the most familiar sense of that term,\nviz. the arithmetical mean; and a single Law of Error, or its\ngraphical equivalent, a Curve of Facility, will suffice accurately\nto indicate the comparative frequency of the different\namounts of the one variable magnitude involved.\n\n3. We may conveniently here again call attention to a\nmisconception or confusion which has been already noticed\nin a former chapter. It is that of confounding the Law of\nError with the Method of Least Squares. These are things\nof an entirely distinct kind. The former is of the nature of\na physical fact, and its production is one which in many\ncases is entirely beyond our control. The latter,--or any\nsimplified application of it, such as the arithmetical average,--is\nno law whatever in the physical sense. It is rather a\nprecept or rule for our guidance. The Law states, in any\ngiven case, how the errors tend to occur in respect of their\nmagnitude and frequency. The Method directs us how to\ntreat these errors when any number of them are presented\nto us. No doubt there is a relation between the two, as will\nbe pointed out in the course of the following pages; but\nthere is nothing really to prevent us from using the same\nmethod for different laws of error, or different methods for\nthe same law. In so doing, the question of distinct right\nand wrong would seldom be involved, but rather one of more\nor less propriety.\n\n4. The reader must understand,--as was implied in\nthe illustration about the pistol shots,--that the ultimate\nproblem before us is an _inverse_ one. That is, we are supposed\nto have a moderate number of 'errors' before us and\nwe are to undertake to say whereabouts is the centre from\nwhich they diverge. This resembles the determination of a\ncause from the observation of an effect. But, as mostly\nhappens in inverse problems, we must commence with the\nconsideration of the direct problem. In other words, so far\nas concerns the case before us, we shall have to begin by\nsupposing that the ultimate object of our aim,--that is, the\ntrue centre of our curve of frequency,--is already known to\nus: in which case all that remains to be done is to study the\nconsequences of taking averages of the magnitudes which\nconstitute the errors.\n\n5. We shall, for the present, confine our remarks to\nwhat must be regarded as the typical case where considerations\nof Probability are concerned; viz. that in which\nthe law of arrangement or development is of the Binomial\nkind. The nature of this law was explained in Chap. II.,\nwhere it was shown that the frequency of the respective\nnumbers of occurrences was regulated in accordance with\nthe magnitude of the successive terms of the expansion of\nthe binomial (1 + 1)^{n}. It was also pointed out that when n becomes\nvery great, that is, when the number of influencing\ncircumstances is very large, and their relative individual\ninfluence correspondingly small, the form assumed by a\ncurve drawn through the summits of ordinates representing\nthese successive terms of the binomial tends towards that\nassigned by the equation y = Ae^{-h^{2}x^{2}}.\n\nFor all practical purposes therefore we may talk indifferently\nof the Binomial or Exponential law; if only on\nthe ground that the arrangement of the actual phenomena\non one or other of these two schemes would soon become\nindistinguishable when the numbers involved are large.\nBut there is another ground than this. Even when the\nphenomena themselves represent a continuous magnitude,\nour measurements of them,--which are all with which we\ncan deal,--are discontinuous. Suppose we had before us the\naccurate heights of a million adult men. For all practical\npurposes these would represent the variations of a continuous\nmagnitude, for the differences between two successive\nmagnitudes, especially near the mean, would be\ninappreciably small. But our tables will probably represent\nthem only to the nearest inch. We have so many assigned\nas 69 inches; so many as 70; and so on. The tabular\nstatement in fact is of much the same character as if we\nwere assigning the number of 'heads' in a toss of a handful\nof pence; that is, as if we were dealing with discontinuous\nnumbers on the binomial, rather than with a continuous\nmagnitude on the exponential arrangement.\n\n6. Confining ourselves then, for the present, to this\ngeneral head, of the binomial or exponential law, we must\ndistinguish two separate cases in respect of the knowledge\nwe may possess as to the generating circumstances of the\nvariable magnitudes.\n\n(1) There is, first, the case in which the conditions of\nthe problem are determinable _\u00e0 priori_: that is, where we are\nable to say, prior to specific experience, how frequently each\ncombination will occur in the long run. In this case the\nmain or ultimate object for which we are supposing that the\naverage is employed,--i.e. that of discovering the true mean\nvalue,--is superseded. We are able to say what the mean\nor central value in the long run will be; and therefore there\nis no occasion to set about determining it, with some trouble\nand uncertainty, from a small number of observations. Still\nit is necessary to discuss this case carefully, because its\nassumption is a necessary link in the reasoning in other\ncases.\n\nThis comparatively _\u00e0 priori_ knowledge may present itself\nin two different degrees as respects its completeness. In the\nfirst place it may, so far as the circumstances in question\nare concerned, be absolutely complete. Consider the results\nwhen a handful of ten pence is repeatedly tossed up. We\nknow precisely what the mean value is here, viz. equal\ndivision of heads and tails: we know also the chance of six\nheads and four tails, and so on. That is, if we had to plot\nout a diagram showing the relative frequency of each combination,\nwe could do so without appealing to experience.\nWe could draw the appropriate binomial curve from the\ngenerating conditions given in the statement of the problem.\n\nBut now consider the results of firing at a target consisting\nof a long and narrow strip, of which one point is\nmarked as the centre of aim.[3] Here (assuming that there\nare no causes at work to produce permanent bias) we know\nthat this centre will correspond to the mean value. And we\nknow also, in a general way, that the dispersion on each side\nof this will follow _a_ binomial law. But if we attempted to\nplot out the proportions, as in the preceding case, by erecting\nordinates which should represent each degree of frequency\nas we receded further from the mean, we should find that\nwe could not do so. Fresh data must be given or inferred.\nA good marksman and a bad marksman will both distribute\ntheir shot according to the same general law; but the\nrapidity with which the shots thin off as we recede from the\ncentre will be different in the two cases. Another 'constant'\nis demanded before the curve of frequency could be correctly\ntraced out.\n\n7. (2) The second division, to be next considered,\ncorresponds for all logical purposes to the first. It comprises\nthe cases in which though we have no \u00e0 priori knowledge\nas to the situation about which the values will tend to\ncluster in the long run, yet we have sufficient experience at\nhand to assign it with practical certainty. Consider for\ninstance the tables of human stature. These are often very\nextensive, including tens or hundreds of thousands. In such\ncases the mean or central value is determinable with just as\ngreat certainty as by any _\u00e0 priori_ rule. That is, if we took\nanother hundred thousand measurements from the same\nclass of population, we should feel secure that the average\nwould not be altered by any magnitude which our measuring\ninstruments could practically appreciate.\n\n8. But the mere assignment of the mean or central\nvalue does not here, any more than in the preceding case,\ngive us all that we want to know. It _might_ so happen that\nthe mean height of two populations was the same, but that\nthe law of dispersion about that mean was very different:\nso that a man who in one series was an exceptional giant or\ndwarf should, in the other, be in no wise remarkable.\n\nTo explain the process of thus determining the actual magnitude of the\ndispersion would demand too much mathematical detail; but some\nindication may be given. What we have to do is to determine the\nconstant h in the equation[4] y = (h/sqrt{\u03c0}) e^{-h^{2} x^{2}}. In\ntechnical language, what we have to do is to determine the _modulus_\nof this equation. The quantity 1/h in the above expression is called\nthe modulus. It measures the degree of contraction or dispersion about\nthe mean indicated by this equation. When it is large the dispersion\nis considerable; that is the magnitudes are not closely crowded up\ntowards the centre, when it is small they are thus crowded up. The\nsmaller the modulus in the curve representing the thickness with which\nthe shot-marks clustered about the centre of the target, the better\nthe marksman.\n\n9. There are several ways of determining the modulus. In the first of\nthe cases discussed above, where our theoretical knowledge is\ncomplete, we are able to calculate it _\u00e0 priori_ from our knowledge of\nthe chances. We should naturally adopt this plan if we were tossing up\na large handful of pence.\n\nThe usual _\u00e0 posteriori_ plan, when we have the measurements\nof the magnitudes or observations before us, is this:--Take\nthe mean square of the errors, and double this; the result\ngives the square of the modulus. Suppose, for instance,\nthat we had the five magnitudes, 4, 5, 6, 7, 8. The mean of\nthese is 6: the 'errors' are respectively 2, 1, 0, 1, 2. Therefore\nthe 'modulus squared' is equal to 10/5; i.e. the modulus is sqrt{2}.\nHad the magnitudes been 2, 4, 6, 8, 10; representing\nthe same mean (6) as before, but displaying a greater dispersion\nabout it, the modulus would have been larger, viz. sqrt{8}\ninstead of sqrt{2}.\n\nMr Galton's method is more of a graphical nature. It\nis described in a paper on Statistics by Intercomparison\n(_Phil. Mag._ 1875), and elsewhere. It may be indicated as\nfollows. Suppose that we were dealing with a large number\nof measurements of human stature, and conceive that all the\npersons in question were marshalled in the order of their\nheight. Select the average height, as marked by the central\nman of the row. Suppose him to be 69 inches. Then raise\n(or depress) the scale from this point until it stands at such\na height as just to include one half of the men above (or\nbelow) the mean. (In practice this would be found to require\nabout 1.71 inches: that is, one quarter of any large\ngroup of such men will fall between 69 and 70.71 inches.)\nDivide this number by 0.4769 and we have the modulus. In\nthe case in question it would be equal to about 3.6 inches.\n\nUnder the assumption with which we start, viz. that the law of error\ndisplays itself in the familiar binomial form, or in some form\napproximating to this, the three methods indicated above will coincide\nin their result. Where there is any doubt on this head, or where we do\nnot feel able to calculate beforehand what will be the rate of\ndispersion, we must adopt the second plan of determining the modulus.\nThis is the only universally applicable mode of calculation: in fact\nthat it should yield the modulus is a truth of definition; for in\ndetermining the error of mean square we are really doing nothing else\nthan determining the modulus, as was pointed out in the last chapter.\n\n10. The position then which we have now reached is this. Taking it for\ngranted that the Law of Error will fall into the symbolic form\nexpressed by the equation y = (h/sqrt{\u03c0}) e^{-h^{2} x^{2}}, we have\nrules at hand by which h may be determined. We therefore, for the\npurposes in question, know all about the curve of frequency: we can\ntrace it out on paper: given one value,--say the central one,--we can\ndetermine any other value at any distance from this. That is, knowing\nhow many men in a million, say, are 69 inches high, we can determine\nwithout direct observation how many will be 67, 68, 70, 71, and so on.\n\nWe can now adequately discuss the principal question of logical\ninterest before us; viz. _why_ do we take averages or means? What is\nthe exact nature and amount of the advantage gained by so doing? The\nadvanced student would of course prefer to work out the answers to\nthese questions by appealing at once to the Law of Error in its\nultimate or exponential form. But I feel convinced that the best\nmethod for those who wish to gain a clear conception of the logical\nnature of the process involved, is to begin by treating it as a\nquestion of combinations such as we are familiar with in elementary\nalgebra; in other words to take a finite number of errors and to see\nwhat comes of averaging these. We can then proceed to work out\narithmetically the results of combining two or more of the errors\ntogether so as to get a new series, not contenting ourselves with the\ngeneral character merely of the new law of error, but actually\ncalculating what it is in the given case. For the sake of simplicity\nwe will not take a series with a very large number of terms in it, but\nit will be well to have enough of them to secure that our law of error\nshall roughly approximate in its form to the standard or exponential\nlaw.\n\nFor this purpose the law of error or divergence given by supposing our\neffort to be affected by ten causes, each of which produces an equal\nerror, but which error is equally likely to be positive and negative\n(or, as it might perhaps be expressed, 'ten equal and indifferently\nadditive and subtractive causes') will suffice. This is the lowest\nnumber formed according to the Binomial law, which will furnish to the\neye a fair indication of the limiting or Exponential law.[5] The whole\nnumber of possible cases here is 2^{10} or 1024; that is, this is the\nnumber required to exhibit not only all the cases which can occur (for\nthere are but eleven really distinct cases), but also the relative\nfrequency with which each of these cases occurs in the long run. Of\nthis total, 252 will be situated at the mean, representing the 'true'\nresult, or that given when five of the causes of disturbance just\nneutralize the other five. Again, 210 will be at what we will call one\nunit's distance from the mean, or that given by six causes combining\nagainst four; and so on; until at the extreme distance of five places\nfrom the mean we get but one result, since in only one case out of the\n1024 will all the causes combine together in the same direction. The\nset of 1024 efforts is therefore a fair representation of the\ndistribution of an infinite number of such efforts. A graphical\nrepresentation of the arrangement is given here.\n\n[Figure: Binomial distribution for the tenth power.]\n\n11. This representing a complete set of single observations or\nefforts, what will be the number and arrangement in the corresponding\nset of combined or reduced observations, say of two together? With\nregard to the number we must bear in mind that this is not a case of\nthe combinations of things which cannot be repeated; for any given\nerror, say the extreme one at F, can obviously be repeated twice\nrunning. Such a repetition would be a piece of very bad luck no doubt,\nbut being possible it must have its place in the set. Now the possible\nnumber of ways of combining 1024 things two together, where the same\nthing may be repeated twice running, is 1024 \u00d7 1024 or 1048576. This\nthen is the number in a complete cycle of the results taken two and\ntwo together.\n\n12. So much for their number; now for their arrangement or\ndistribution. What we have to ascertain is, firstly, how many times\neach possible pair of observations will present itself; and, secondly,\nwhere the new results, obtained from the combination of each pair, are\nto be placed. With regard to the first of these enquiries;--it will be\nreadily seen that on one occasion we shall have F repeated twice; on\n20 occasions we shall have F combined with E (for F coming first we\nmay have it followed by any one of the 10 at E, or any one of these\nmay be followed by F); E can be repeated in 10 \u00d7 10, or 100 ways, and\nso on.\n\nNow for the position of each of these reduced observations, the\nrelative frequency of whose component elements has thus been pointed\nout. This is easy to determine, for when we take two errors there is\n(as was seen) scarcely any other mode of treatment than that of\nselecting the mid-point between them; this mid-point of course\nbecoming identical with each of them when the two happen to\ncoincide. It will be seen therefore that F will recur once on the new\narrangement, viz. by its being repeated twice on the old one. G midway\nbetween E and F, will be given 20 times. E, on our new arrangement,\ncan be got at in two ways, viz. by its being repeated twice (which\nwill happen 100 times), and by its being obtained as the mid-point\nbetween D and F (which will happen 90 times). Hence E will occur 190\ntimes altogether.\n\nThe reader who chooses to take the trouble may work out the frequency\nof all possible occurrences in this way, and if the object were simply\nto illustrate the principle in accordance with which they occur, this\nmight be the best way of proceeding. But as he may soon be able to\nobserve, and as the mathematician would at once be able to prove, the\nnew 'law of facility of error' can be got at more quickly deductively,\nviz. by taking the successive terms of the expansion of (1 + 1)^{20}.\nThey are given, below the line, in the figure on p. 476.\n\n13. There are two apparent obstacles to any direct comparison between\nthe distribution of the old set of simple observations, and the new\nset of combined or reduced ones. In the first place, the number of\nthe latter is much greater. This, however, is readily met by reducing\nthem both to the same scale, that is by making the same total number\nof each. In the second place, half of the new positions have no\nrepresentatives amongst the old, viz. those which occur midway between\nF and E, E and D, and so on. This can be met by the usual plan of\ninterpolation, viz. by filling in such gaps by estimating what would\nhave been the number at the missing points, on the same scale, had\nthey been occupied. Draw a curve through the vertices of the\nordinates at A, B, C, &c., and the lengths of the ordinates at the\nintermediate points will very fairly represent the corresponding\nfrequency of the errors of those magnitudes respectively. When the\ngaps are thus filled up, and the numbers thus reduced to the same\nscale, we have a perfectly fair basis of comparison. (See figure on\nnext page.)\n\nSimilarly we might proceed to group or 'reduce' three observations, or\nany greater number. The number of possible groupings naturally becomes\nvery much larger, being (1024)^{3} when they are taken three\ntogether. As soon as we get to three or more observations, we have (as\nalready pointed out) a variety of possible modes of treatment or\nreduction, of which that of taking the arithmetical mean is but one.\n\n14. The following figure is intended to illustrate the nature of the\nadvantage secured by thus taking the arithmetical mean of several\nobservations.\n\nThe curve ABCD represents the arrangement of a given number of\n'errors' supposed to be disposed according to the binomial law already\nmentioned, when the angles have been smoothed off by drawing a curve\nthrough them. A'CD' represents the similar arrangement of the same\nnumber when given not as simple errors, but as averages of pairs of\nerrors. A\"BD\", again, represents the similar arrangement obtained as\naverages of errors taken three together. They are drawn as carefully\nto scale as the small size of the figure permits.\n\n[Figure: Gaussian distributions for two or three observations.]\n\n15. A glance at the above figure will explain to the reader, better\nthan any verbal description, the full significance of the statement\nthat the result of combining two or more measurements or observations\ntogether and taking the average of them, instead of stopping short at\nthe single elements, is to make large errors comparatively more\nscarce. The advantage is of the same general description as that of\nfishing in a lake where, of the same number of fish, there are more\nbig and fewer little ones than in another water: of dipping in a bag\nwhere of the same number of coins there are more sovereigns and fewer\nshillings; and so on. The extreme importance, however, of obtaining a\nperfectly clear conception of the subject may render it desirable to\nwork this out a little more fully in detail.\n\nFor one thing, then, it must be clearly understood that the result of\na set of 'averages' of errors is nothing else than another set of\n'errors,' No device can make the attainment of the true result\ncertain,--to suppose the contrary would be to misconceive the very\nfoundations of Probability,--no device even can obviate the\npossibility of being actually worse off as the result of our\nlabour. The average of two, three, or any larger number of single\nresults, may give a worse result, i.e. one further from the ultimate\naverage, than was given by the first observation we made. We must\nsimply fall back upon the justification that big deviations are\nrendered scarcer in the long run.\n\nAgain; it may be pointed out that though, in the above investigation,\nwe have spoken only of the arithmetical average as commonly understood\nand employed, the same general results would be obtained by resorting\nto almost any symmetrical and regular mode of combining our\nobservations or errors. The two main features of the regularity\ndisplayed by the Binomial Law of facility were (1) ultimate symmetry\nabout the central or true result, and (2) increasing relative\nfrequency as this centre was approached. A very little consideration\nwill show that it is no peculiar prerogative of the arithmetical mean\nto retain the former of these and to increase the latter. In saying\nthis, however, a distinction must be attended to for which it will be\nconvenient to refer to a figure.\n\n16. Suppose that O, in the line D'OD, was the point aimed at by any\nseries of measurements; or, what comes to the same thing for our\npresent purpose, was the ultimate average of all the measurements\nmade. What we mean by a symmetrical arrangement of the values in\nregard to O, is that for every error OB, there shall be in the long\nrun a precisely corresponding opposite one OB'; so that when we erect\nthe ordinate BQ, indicating the frequency with which B is yielded, we\nmust erect an equal one B'Q'. Accordingly the two halves of the curve\non each side of P, viz. PQ and PQ' are precisely alike.\n\n[Figure: Symmetry of a distribution.]\n\nIt then readily follows that the secondary curve, viz. that marking\nthe law of frequency of the averages of two or more simple errors,\nwill also be symmetrical. Consider any three points B, C, D: to these\ncorrespond another three B', C', D'. It is obvious therefore that any\nregular and symmetrical mode of dealing with all the groups, of which\nBCD is a sample, will result in symmetrical arrangement about the\ncentre O. The ordinary familiar arithmetical average is but one out of\nmany such modes. One way of describing it is by saying that the\naverage of B, C, D, is assigned by choosing a point such that the sum\nof the squares of its distances from B, C, D, is a minimum. But we\nmight have selected a point such that the cubes, or the fourth powers,\nor any higher powers should be a minimum. These would all yield curves\nresembling in a general way the dotted line in our figure. Of course\nthere would be insuperable practical objections to any such courses as\nthese; for the labour of calculation would be enormous, and the\nresults so far from being better would be worse than those afforded by\nthe employment of the ordinary average. But so far as concerns the\ngeneral principle of dealing with discordant and erroneous results, it\nmust be remembered that the familiar average is but one out of\ninnumerable possible resources, all of which would yield the same sort\nof help.\n\n17. Once more. We saw that a resort to the average had the effect of\n'humping up' our curve more towards the centre, expressive of the fact\nthat the errors of averages are of a better, i.e. smaller kind. But it\nmust be noticed that exactly the same characteristics will follow, as\na general rule, from any other such mode of dealing with the\nindividual errors. No strict proof of this fact can be given here, but\na reference to one of the familiar results of taking combinations of\nthings will show whence this tendency arises. Extreme results, as\nyielded by an average of any kind, can only be got in one way, viz. by\nrepetitions of extremes in the individuals from which the averages\nwere obtained. But intermediate results can be got at in two ways,\nviz. either by intermediate individuals, or by combinations of\nindividuals in opposite directions. In the case of the Binomial Law of\nError this tendency to thicken towards the centre was already strongly\npredominant in the individual values before we took them in hand for\nour average; but owing to this characteristic of combinations we may\nlay it down (broadly speaking) that any sort of average applied to any\nsort of law of distribution will give a result which bears the same\ngeneral relation to the individual values that the dotted lines above\nbear to the black line.[6]\n\n18. This being so, the speculative advantages of one method of\ncombining, or averaging, or reducing, our observations, over another\nmethod,--irrespective, that is, of the practical conveniences in\ncarrying them out,--will consist solely in the degree of rapidity with\nwhich it tends thus to cluster the result about the centre. We shall\nhave to subject this merit to a somewhat further analysis, but for the\npresent purpose it will suffice to say that if one kind of average\ngave the higher dotted line in the figure on p. 479 and another gave\nthe lower dotted line, we should say that the former was the better\none. The advantage is of the same general kind as that which is\nfurnished in algebraical calculation, by a series which converges\nrapidly towards the true value as compared with one which converges\nslowly. We can do the work sooner or later by the aid of either; but\nwe get nearer the truth by the same amount of labour, or get as near\nby a less amount of labour, on one plan than on the other.\n\nAs we are here considering the case in which the individual\nobservations are supposed to be grouped in accordance with the\nBinomial Law, it will suffice to say that in this case there is no\ndoubt that the arithmetical average is not only the simplest and\neasiest to deal with, but is also the best in the above sense of the\nterm. And since this Binomial Law, or something approximating to it,\nis of very wide prevalence, a strong _prim\u00e2 facie_ case is made out\nfor the general employment of the familiar average.\n\n19. The analysis of a few pages back carried the results of the\naveraging process as far as could be conveniently done by the help of\nmere arithmetic. To go further we must appeal to higher mathematics,\nbut the following indication of the sort of results obtained will\nsuffice for our present purpose. After all, the successive steps,\nthough demanding intricate reasoning for their proof, are nothing more\nthan generalizations of processes which could be established by simple\narithmetic.[7] Briefly, what we do is this:--\n\n(1) We first extend the proof from the binomial form, with its finite\nnumber of elements, to the limiting or exponential form. Instead of\nconfining ourselves to a small number of discrete errors, we then\nrecognize the possibility of any number of errors of any magnitude\nwhatever.\n\n(2) In the next place, instead of confining ourselves to the\nconsideration of an average of two or three only,--already, as we have\nseen, a tedious piece of arithmetic,--we calculate the result of an\naverage of any number, n. The actual result is extremely simple. If\nthe modulus of the single errors is c, that of the average of n of\nthese will be c \u00f7 sqrt{n}.\n\n(3) Finally we draw similar conclusions in reference to the _sum or\ndifference_ of two averages of any numbers. Suppose, for instance,\nthat m errors were first taken and averaged, and then n similarly\ntaken and averaged. These averages will be nearly, but not quite,\nequal. Their sum or difference,--these, of course, are\nindistinguishable in the end, since positive and negative errors are\nsupposed to be equal and opposite,--will itself be an 'error', every\nmagnitude of which will have a certain assignable probability or\nfacility of occurrence. What we do is to assign the modulus of _these_\nerrors. The actual result again is simple. If c had been the modulus\nof the single errors, that of the sum or difference of the averages of\nm and n of them will be c sqrt{1/m + 1/n}.\n\n20. So far, the problem under investigation has been of a direct\nkind. We have supposed that the ultimate mean value or central\nposition has been given to us; either _\u00e0 priori_ (as in many games of\nchance), or from more immediate physical considerations (as in aiming\nat a mark), or from extensive statistics (as in tables of human\nstature). In all such cases therefore the main desideratum is already\ntaken for granted, and it may reasonably be asked what remains to be\ndone. The answers are various. For one thing we may want to estimate\nthe value of an average of many when compared with an average of a\nfew. Suppose that one man has collected statistics including 1000\ninstances, and another has collected 4000 similar instances. Common\nsense can recognize that the latter are better than the former; but it\nhas no idea _how much_ better they are. Here, as elsewhere,\nquantitative precision is the privilege of science. The answer we\nreceive from this quarter is that, in the long run, the modulus,--and\nwith this the probable error, the mean error, and the error of mean\nsquare, which all vary in proportion,--diminishes inversely as the\nsquare root of the number of measurements or observations. (This\nfollows from the second of the above formul\u00e6.) Accordingly the\nprobable error of the more extensive statistics here is one half that\nof the less extensive. Take another instance. Observation shows that\n\"the mean height of 2,315 criminals differs from the mean height of\n8,585 members of the general adult population by about two inches\"\n(v. Edgeworth, Methods of Statistics: _Stat. Soc. Journ._ 1885). As\nbefore, common sense would feel little doubt that such a difference\nwas significant, but it could give no numerical estimate of the\nsignificance. Appealing to science, we see that this is an\nillustration of the third of the above formul\u00e6. What we really want to\nknow is the odds against the averages of two large batches differing\nby an assigned amount: in this case by an amount equalling twenty-five\ntimes the modulus of the variable quantity. The odds against this are\nmany billions to one.\n\n21. The number of direct problems which will thus admit of solution is\nvery great, but we must confine ourselves here to the main inverse\nproblem to which the foregoing discussion is a preliminary. It is\nthis. Given _a few only_ of one of these groups of measurements or\nobservations; what can we do with these, in the way of determining\nthat mean about which they would ultimately be found to cluster?\nGiven a large number of them, they would betray the position of their\nultimate centre with constantly increasing certainty: but we are now\nsupposing that there are only a few of them at hand, say half a dozen,\nand that we have no power at present to add to the number.\n\nIn other words,--expressing ourselves by the aid of graphical\nillustration, which is perhaps the best method for the novice and for\nthe logical student,--in the direct problem we merely have to draw the\ncurve of frequency from a knowledge of its determining elements;\nviz. the position of the centre, and the numerical value of the\nmodulus. In the inverse problem, on the other hand, we have three\nelements at least, to determine. For not only must we, (1), as before,\ndetermine whereabouts the centre may be assumed to lie; and (2), as\nbefore, determine the value of the modulus or degree of dispersion\nabout this centre. This does not complete our knowledge. Since neither\nof these two elements is assigned with certainty, we want what is\nalways required in the Theory of Chances, viz. some estimate of their\nprobable truth. That is, after making the best assignment we can as to\nthe value of these elements, we want also to assign numerically the\n'probable error' committed in such assignment. Nothing more than this\ncan be attained in Probability, but nothing less than this should be\nset before us.\n\n22. (1) As regards the first of these questions, the answer is very\nsimple. Whether the number of measurements or observations be few or\nmany, we must make the assumption that their average _is_ the point we\nwant; that is, that the average of the few will coincide with the\nultimate average. This is the best, in fact the only assumption we can\nmake. We should adopt this plan, of course, in the extreme case of\nthere being only _one_ value before us, by just taking that one; and\nour confidence increases slowly with the number of values before\nus. The only difference therefore here between knowledge resting upon\nsuch data, and knowledge resting upon complete data, lies not in the\nresult obtained but in the confidence with which we entertain it.\n\n23. (2) As regards the second question, viz. the determination of the\nmodulus or degree of dispersion about the mean, much the same may be\nsaid. That is, we adopt the same rule for the determination of the\nE.M.S. (error of mean square) by which the modulus is assigned, as we\nshould adopt if we possessed full Information. Or rather we are\nconfined to _one_ of the rules given on p. 473, viz. the second, for\nby supposition we have neither the _\u00e0 priori_ knowledge which would be\nable to supply the first, nor a sufficient number of observations to\njustify the third. That is, we reckon the errors, measured from the\naverage, and calculate their mean square: twice this is equal to the\nsquare of the modulus of the probable curve of facility.[8]\n\n24. (3) The third question demands for its solution somewhat advanced\nmathematics; but the results can be indicated without much\ndifficulty. A popular way of stating our requirement would be to say\nthat we want to know how likely it is that the mean of the few, which\nwe have thus accepted, shall coincide with the true mean. But this\nwould be to speak loosely, for the chances are of course indefinitely\ngreat against such precise coincidence. What we really do is to assign\nthe 'probable error'; that is, to assign a limit which it is as likely\nas not that the discrepancy between the inferred mean and the true\nmean should exceed.[9] To take a numerical example: suppose we had\nmade several measurements of a wall with a tape, and that the average\nof these was 150 feet. The scrupulous surveyor would give us this\nresult, with some such correction as this added,--'probable error 3\ninches'. All that this means is that we may assume that the true value\nis 150 feet, with a confidence that in half the cases (of this\ndescription) in which we did so, we should really be within three\ninches of the truth.\n\nThe expression for this probable error is a simple multiple of the\nmodulus: it is the modulus multiplied by 0.4769.... That it should be\nsome function of the modulus, or E.M.S., seems plausible enough; for\nthe greater the errors,--in other words the wider the observed\ndiscrepancy amongst our measurements,--the less must be the confidence\nwe can feel in the accuracy of our determination of the mean. But, of\ncourse, without mathematics we should be quite unable to attempt any\nnumerical assignment.\n\n25. The general conclusion therefore is that the determination of the\ncurve of facility,--and therefore ultimately of every conclusion which\nrests upon a knowledge of this curve,--where only a few observations\nare available, is of just the same kind as where an infinity are\navailable. The rules for obtaining it are the same, but the confidence\nwith which it can be accepted is less.\n\nThe knowledge, therefore, obtainable by an average of a small number\nof measurements of any kind, hardly differs except in degree from that\nwhich would be attainable by an indefinitely extensive series of\nthem. We know the same sort of facts, only we are less certain about\nthem. But, on the other hand, the knowledge yielded by an average even\nof a small number differs in kind from that which is yielded by a\nsingle measurement. Revert to our marksman, whose bullseye is supposed\nto have been afterwards removed. If he had fired only a single shot,\nnot only should we be less certain of the point he had aimed at, but\nwe should have no means whatever of guessing at the quality of his\nshooting, or of inferring in consequence anything about the probable\nremoteness of the next shot from that which had gone before. But\ndirectly we have a plurality of shots before us, we not merely feel\nmore confident as to whereabouts the centre of aim was, but we also\ngain some knowledge as to how the future shots will cluster about the\nspot thus indicated. The quality of his shooting begins at once to be\nbetrayed by the results.\n\n26. Thus far we have been supposing the Law of Facility to be of the\nBinomial type. There are several reasons for discussing this at such\ncomparative length. For one thing it is the only type which,--or\nsomething approximately resembling which,--is actually prevalent over\na wide range of phenomena. Then again, in spite of its apparent\nintricacy, it is really one of the simplest to deal with; owing to the\nfact that every curve of facility derived from it by taking averages\nsimply repeats the same type again. The curve of the average only\ndiffers from that of the single elements in having a smaller modulus;\nand its modulus is smaller in a ratio which is exceedingly easy to\ngive. If that of the one is c, that of the other (derived by averaging\nn single elements) is c/sqrt{n}.\n\nBut for understanding the theory of averages we must consider other\ncases as well. Take then one which is intrinsically as simple as it\npossibly can be, viz. that in which all values within certain assigned\nlimits are equally probable. This is a case familiar enough in\nabstract Probability, though, as just remarked, not so common in\nnatural phenomena. It is the state of things when we act at random\ndirectly upon the objects of choice;[10] as when, for instance, we\nchoose digits at random out of a table of logarithms.\n\nThe reader who likes to do so can without much labour work out the\nresult of taking an average of two or three results by proceeding in\nexactly the same way which we adopted on p. 476. The 'curve of\nfacility' with which we have to start in this case has become of\ncourse simply a finite straight line. Treating the question as one of\nsimple combinations, we may divide the line into a number of equal\nparts, by equidistant points; and then proceed to take these two and\ntwo together in every possible way, as we did in the case discussed\nsome pages back.\n\nIf we did so, what we should find would be this. When an average of\n_two_ is taken, the 'curve of facility' of the average becomes a\ntriangle with the initial straight line for base; so that the ultimate\nmean or central point becomes the likeliest result even with this\ncommencement of the averaging process. If we were to take averages of\nthree, four, and so on, what we should find would be that the Binomial\nlaw begins to display itself here. The familiar bell shape of the\nexponential curve would be more and more closely approximated to,\nuntil we obtained something quite indistinguishable from it.\n\n27. The conclusion therefore is that when we are dealing with averages\ninvolving a considerable number it is not necessary, in general, to\npresuppose the binomial law of distribution in our original data. The\nlaw of arrangement of what we may call the derived curve, viz. that\ncorresponding to the averages, will not be appreciably affected\nthereby. Accordingly we seem to be justified in bringing to bear all\nthe same apparatus of calculation as in the former case. We take the\ninitial average as the probable position of the true centre or\nultimate average: we estimate the probability that we are within an\nassignable distance of the truth in so doing by calculating the 'error\nof mean square'; and we appeal to this same element to determine the\nmodulus, i.e. the amount of contraction or dispersion, of our derived\ncurve of facility.\n\nThe same general considerations will apply to most other kinds of Law\nof Facility. Broadly speaking,--we shall come to the examination of\ncertain exceptions immediately,--whatever may have been the primitive\narrangement (i.e. that of the single results) the arrangement of the\nderived results (i.e. that of the averages) will be more crowded up\ntowards the centre. This follows from the characteristic of\ncombinations already noticed, viz. that extreme values can only be got\nat by a repetition of several extremes, whereas intermediate values\ncan be got at either by repetition of intermediates or through the\ncounteraction of opposite extremes. Provided the original\ndistribution be symmetrical about the centre, and provided the limits\nof possible error be finite, or if infinite, that the falling off of\nfrequency as we recede from the mean be very rapid, then the results\nof taking averages will be better than those of trusting to single\nresults.\n\n28. We will now take notice of an exceptional case. We shall do so,\nnot because it is one which can often actually occur, but because the\nconsideration of it will force us to ask ourselves with some\nminuteness what we mean in the above instances by calling the results\nof the averages 'better' than those of the individual values. A\ndiagram will bring home to us the point of the difficulty better than\nany verbal or symbolic description.\n\n[Figure: Distribution for two samples from a non-Gaussian distribution.]\n\nThe black line represents a Law of Error easily stated in words, and\none which, as we shall subsequently see, can be conceived as occurring\nin practice. It represents a state of things under which up to a\ncertain distance from O, on each side, viz. to A and B, the\nprobability of an error diminishes uniformly with the distance from O;\nwhilst beyond these points, up to E and F, the probability of error\nremains constant. The dotted line represents the resultant Law of\nError obtained by taking the average of the former two and two\ntogether. Now is the latter 'better' than the former?  Under it,\ncertainly, great errors are less frequent and intermediate ones more\nfrequent; but then on the other hand the _small_ errors are less\nfrequent: is this state of things on the whole an improvement or not?\nThis requires us to reconsider the whole question.\n\n29. In all the cases discussed in the previous sections the\nsuperiority of the curve of averages over that of the single results\nshowed itself at every point. The big errors were scarcer and the\nsmall errors were commoner; it was only just at one intermediate point\nthat the two were on terms of equality, and this point was not\nsupposed to possess any particular significance or\nimportance. Accordingly we had no occasion to analyse the various\ncases included under the general relation. It was enough to say that\none was better than the other, and it was sufficient for all purposes\nto take the 'modulus' as the measure of this superiority. In fact we\nare quite safe in simply saying that the _average_ of those average\nresults is better than that of the individual ones.\n\nWhen however we proceed in what Hume calls \"the sifting humour,\" and\nenquire _why_ it is sufficient thus to trust to the average; we find,\nin addition to the considerations hitherto advanced, that some\npostulate was required as to the _consequences_ of the errors we\nincur. It involved an estimate of what is sometimes called the\n'detriment' of an error. It seemed to take for granted that large and\nsmall errors all stand upon the same general footing of being\nmischievous in their consequences, but that their evil effects\nincrease in a greater ratio than that of their own magnitude.\n\n30. Suppose, for comparison, a case in which the importance of an\nerror is directly proportional to its magnitude (of course we suppose\npositive and negative errors to balance each other in the long run):\nit does not appear that any advantage would be gained by taking\naverages. Something of this sort may be considered to prevail in cases\nof mere purchase and sale. Suppose that any one had to buy a very\nlarge number of yards of cloth at a constant price per yard: that he\nhad to do this, say, five times a day for many days in succession. And\nconceive that the measurement of the cloth was roughly estimated on\neach separate occasion, with resultant errors which are as likely to\nbe in excess as in defect. Would it make the slightest difference to\nhim whether he paid separately for each piece; or whether the five\nestimated lengths were added together, their average taken, and he\nwere charged with this average price for each piece? In the latter\ncase the errors which will be made in the estimation of each piece\nwill of course be less in the long run than they would be in the\nformer: will this be of any consequence? The answer surely is that it\nwill not make the slightest difference to either party in the\nbargain. In the long run, since the same parties are concerned, it\nwill not matter whether the intermediate errors have been small or\nlarge.\n\nOf course nothing of this sort can be regarded as the general rule. In\nalmost every case in which we have to make measurements we shall find\nthat large errors are much more mischievous than small ones, that is,\nmischievous in a greater ratio than that of their mere magnitude. Even\nin purchase and sale, where _different_ purchasers are concerned, this\nmust be so, for the pleasure of him who is overserved will hardly\nequal the pain of him who is underserved. And in many cases of\nscientific measurement large errors may be simply fatal, in the sense\nthat if there were no reasonable prospect of avoiding them we should\nnot care to undertake the measurement at all.\n\n31. If we were only concerned with practical considerations we might\nstop at this point; but if we want to realize the full logical import\nof average-taking as a means to this particular end, viz. of\nestimating some assigned magnitude, we must look more closely into\nsuch an exceptional case as that which was indicated in the figure on\np. 493. What we there assumed was a state of things in reference to\nwhich extremely small errors were very frequent, but that when once we\ngot beyond a certain small range all other errors, within considerable\nlimits, were equally likely.\n\nIt is not difficult to imagine an example which will aptly illustrate\nthe case in point: at worst it may seem a little far-fetched.\nConceive then that some firm in England received a hurried order to\nsupply a portion of a machine, say a steam-engine, to customers at a\ndistant place; and that it was absolutely essential that the work\nshould be true to the tenth of an inch for it to be of any use. But\nconceive also that two specifications had been sent, resting on\ndifferent measurements, in one of which the length of the requisite\npiece was described as sixty and in the other sixty-one inches. On the\nassumption of any ordinary law of error, whether of the binomial type\nor not, there can be no doubt that the firm would make the best of a\nvery bad job by constructing a piece of 60 inches and a half:\ni.e. they would have a better chance of being within the requisite\ntenth of an inch by so doing, than by taking either of the two\nspecifications at random and constructing it accurately to this. But\nif the law were of the kind indicated in our diagram,[11] then it\nseems equally certain that they would be less likely to be within the\nrequisite narrow margin by so doing. As a mere question of\nprobability,--that is, if such estimates were acted upon again and\nagain,--there would be fewer failures encountered by simply choosing\none of the conflicting measurements at random and working exactly to\nthis, than by trusting to the average of the two.\n\nThis suggests some further reflections as to the taking of\naverages. We will turn now to another exceptional case,\nbut one involving somewhat different considerations than\nthose which have been just discussed. As before, it may be\nmost conveniently introduced by commencing with an example.\n\n32. Suppose then that two scouts were sent to take the calibre of a\ngun in a hostile fort,--we may conceive that the fort was to be\noccupied next day, and used against the enemy, and that it was\nimportant to have a supply of shot or shell,--and that the result is\nthat one of them reports the calibre to be 8 inches and the other 9.\nWould it be wise to assume that the mean of these two, viz. 8-1/2\ninches, was a likelier value than either separately?\n\nThe answer seems to be this. If we have reason to suppose that the\npossible calibres partake of the nature of a _continuous_\nmagnitude,--i.e. that all values, with certain limits, are to be\nconsidered as admissible, (an assumption which we always make in our\nordinary inverse step from an observation or magnitude to the thing\nobserved or measured)--then we should be justified in selecting the\naverage as the likelier value. But if, on the other hand, we had\nreason to suppose that _whole_ inches are always or generally\npreferred, as is in fact the case now with heavy guns, we should do\nbetter to take, even at hazard, one of the two estimates set before\nus, and trust this alone instead of taking an average of the two.\n\n33. The principle upon which we act here may be stated thus. Just as\nin the direct process of calculating or displaying the 'errors',\nwhether in an algebraic formula or in a diagram, we generally assume\nthat their possibility is continuous, i.e. that all intermediate\nvalues are possible; so, in the inverse process of determining the\nprobable position of the original from the known value of two or more\nerrors, we assume that that position is capable of falling at any\npoint whatever between certain limits. In such an example as the\nabove, where we know or suspect a discontinuity of that possibility of\nposition, the value of the average may be entirely destroyed.\n\nIn the above example we were supposed to know that the calibre of the\nguns was likely to run in English inches or in some other recognized\nunits. But if the battery were in China or Japan, and we knew nothing\nof the standards of length in use there, we could no longer appeal to\nthis principle. It is doubtless highly probable that those calibres\nare not of the nature of continuously varying magnitudes; but in an\nentire ignorance of the standards actually adopted, we are to all\nintents and purposes in the same position as if they were of that\ncontinuous nature. When this is so the objections to trusting to the\naverage would no longer hold good, and if we had only one opportunity,\nor a very few opportunities, we should do best to adhere to the\ncustomary practice.\n\n34. When however we are able to collect and compare a large number of\nmeasurements of various objects, this consideration of the probable\ndiscontinuity of the objects we thus measure,--that is, their tendency\nto assume some one or other of a finite number of distinct magnitudes,\ninstead of showing an equal readiness to adapt themselves to all\nintermediate values,--again assumes importance. In fact, given a\nsufficient number of measurable objects, we can actually deduce with\nmuch probability the standard according to which the things in\nquestion were made.\n\nThis is the problem which Mr Flinders Petrie has attacked with so much\nacuteness and industry in his work on _Inductive Metrology_, a work\nwhich, merely on the ground of its speculative interest, may well be\ncommended to the student of Probability. The main principles on which\nthe reasoning is based are these two:--(1) that all artificers are\nprone to construct their works according to round numbers, or simple\nfractions, of their units of measurement; and (2) that, aiming to\nsecure this, they will stray from it in tolerable accordance with the\nlaw of error. The result of these two assumptions is that if we\ncollect a very large number of measurements of the different parts and\nproportions of some ancient building,--say an Egyptian temple,--whilst\nno assignable length is likely to be permanently unrepresented, yet we\nfind a marked tendency for the measurements to cluster about certain\ndeterminate points in our own, or any other standard scale of\nmeasurement. These points mark the length of the standard, or of some\nmultiple or submultiple of the standard, employed by the old\nbuilders. It need hardly be said that there are a multitude of\npractical considerations to be taken into account before this method\ncan be expected to give trustworthy results, but the leading\nprinciples upon which it rests are comparatively simple.\n\n35. The case just considered is really nothing else than the\nrecurrence, under a different application, of one which occupied our\nattention at a very early stage. We noticed (Chap. II.) the\npossibility of a curve of facility which instead of having a single\nvertex like that corresponding to the common law of error, should\ndisplay two humps or vertices. It can readily be shown that this\nproblem of the measurements of ancient buildings, is nothing more than\nthe reopening of the same question, in a slightly more complex form,\nin reference to the question of the functions of an average.\n\nTake a simple example. Suppose an instance in which great errors, of a\ncertain approximate magnitude, are distinctly more likely to be\ncommitted than small ones, so that the curve of facility, instead of\nrising into one peak towards the centre, as in that of the familiar\nlaw of error, shows a depression or valley there. Imagine, in fact,\ntwo binomial curves, with a short interval between their centres. Now\nif we were to calculate the result of taking averages here we should\nfind that this at once tends to fill up the valley; and if we went on\nlong enough, that is, if we kept on taking averages of sufficiently\nlarge numbers, a peak would begin to arise in the centre. In fact the\nfamiliar single binomial curve would begin to make its appearance.\n\n36. The question then at once suggests itself, ought we to do this?\nShall we give the average free play to perform its allotted function\nof thus crowding things up towards the centre? To answer this question\nwe must introduce a distinction. If that peculiar double-peaked curve\nhad been, as it conceivably might, a true error-curve,--that is, if it\nhad represented the divergences actually made in aiming at the real\ncentre,--the result would be just what we should want. It would\nfurnish an instance of the advantages to be gained by taking averages\neven in circumstances which were originally unfavourable. It is not\ndifficult to suggest an appropriate illustration. Suppose a man firing\nat a mark from some sheltered spot, but such that the range crossed a\nbroad exposed valley up or down which a strong wind was generally\nblowing. If the shot-marks were observed we should find them\nclustering about two centres to the right and left of the\nbullseye. And if the results were plotted out in a curve they would\nyield such a double-peaked curve as we have described. But if the\nwinds were equally strong and prevalent in opposite directions, we\nshould find that the averaging process redressed the consequent\ndisturbance.\n\nIf however the curve represented, as it is decidedly more likely to\ndo, some outcome of natural phenomena in which there was, so to say, a\nreal double aim on the part of nature, it would be otherwise. Take,\nfor instance, the results of measuring a large number of people who\nbelonged to two very heterogeneous races. The curve of facility would\nhere be of the kind indicated on p. 45, and if the numbers of the two\ncommingled races were equal it would display a pair of twin\npeaks. Again the question arises, 'ought' we to involve the whole\nrange within the scope of a single average?  The answer is that the\nobligation depends upon the purpose we have in view. If we want to\ncompare that heterogeneous race, as a whole, with some other, or with\nitself at some other time, we shall do well to average without\nanalysis. All statistics of population, as we have already seen\n(v. p. 47), are forced to neglect a multitude of discriminating\ncharacteristics of the kind in question. But if our object were to\ninterpret the causes of this abnormal error-curve we should do well to\nbreak up the statistics into corresponding parts, and subject these to\nanalysis separately.\n\nSimilarly with the measurements of the ancient buildings. In this\ncase if all our various 'errors' were thrown together into one group\nof statistics we should find that the resultant curve of facility\ndisplayed, not two peaks only, but a succession of them; and these of\nvarious magnitudes, corresponding to the frequency of occurrence of\neach particular measurement. We _might_ take an average of the whole,\nbut hardly any rational purpose could be subserved in so doing;\nwhereas each separate point of maximum frequency of occurrence has\nsomething significant to teach us.\n\n37. One other peculiar case may be noticed in conclusion. Suppose a\ndistinctly asymmetrical, or lop-sided curve of facility, such as\nthis:--\n\n[Figure: An asymmetric (lop-sided) distribution.]\n\nLaws of error, of which this is a graphical representation, are, I\napprehend, far from uncommon. The curve in question, is, in fact, but\na slight exaggeration of that of barometrical heights as referred to\nin the last chapter; when it was explained that in such cases the\nmean, the median, and the maximum ordinate would show a mutual\ndivergence. The doubt here is not, as in the preceding instances,\nwhether or not a single average should be taken, but rather what kind\nof average should be selected. As before, the answer must depend upon\nthe special purpose we have in view. For all ordinary purposes of\ncomparison between one time or place and another, any average will\nanswer, and we should therefore naturally take the arithmetical, as\nthe most familiar, or the median, as the simplest.\n\n38. Cases might however arise under which other kinds of average could\njustify themselves, with a momentary notice of which we may now\nconclude. Suppose, for instance, that the question involved here were\none of desirability of climate. The ordinary mean, depending as it\ndoes so largely upon the number and magnitude of extreme values, might\nvery reasonably be considered a less appropriate test than that of\njudging simply by the relatively most frequent value: in other words,\nby the maximum ordinate. And various other points of view can be\nsuggested in respect of which this particular value would be the most\nsuitable and significant.\n\nIn the foregoing case, viz. that of the weather curve, there was no\nobjective or 'true' value aimed at. But a curve closely resembling\nthis would be representative of that particular class of estimates\nindicated by Mr Galton, and for which, as he has pointed out, the\n_geometrical_ mean becomes the only appropriate one. In this case the\ncurve of facility ends abruptly at O: it resembles a much\nforeshortened modification of the common exponential form. Its\ncharacteristics have been discussed in the paper by Dr Macalister\nalready referred to, but any attempt to examine its properties here\nwould lead us into far too intricate details.\n\n39. The general conclusion from all this seems quite in accordance\nwith the nature and functions of an average as pointed out in the last\nchapter. Every average, it was urged, is but a single representative\nintermediate value substituted for a plurality of actual values. It\nmust accordingly let slip the bulk of the information involved in\nthese latter. Occasionally, as in most ordinary measurements, the one\nthing which it represents is obviously the thing we are in want of;\nand then the only question can be, which mean will most accord with\nthe 'true' value we are seeking. But when, as may happen in most of\nthe common applications of statistics, there is really no 'true value'\nof an objective kind behind the phenomena, the problem may branch out\nin various directions. We may have a variety of purposes to work out,\nand these may demand some discrimination as regards the average most\nappropriate for them. Whenever therefore we have any doubt whether the\nfamiliar arithmetical average is suitable for the purpose in hand we\nmust first decide precisely what that purpose is.\n\n\n1. Mr Mansfield Merriman published in 1877 (_Trans. of the Connecticut\n  Acad._) a list of 408 writings on the subject of Least Squares.\n\n2. In other words, we are to take the \"centre of gravity\" of the\n  shot-marks, regarding them as all of equal weight. This is, in\n  reality, the 'average' of all the marks, as the elementary\n  geometrical construction for obtaining the centre of gravity of a\n  system of points will show; but it is not familiarly so regarded. Of\n  course, when we are dealing with such cases as occur in Mensuration,\n  where we have to combine or reconcile three or more inconsistent\n  equations, some such rule as that of Least Squares becomes\n  imperative. No taking of an average will get us out of the\n  difficulty.\n\n3. The only reason for supposing this exceptional shape is to secure\n  simplicity. The ordinary target, allowing errors in two dimensions,\n  would yield slightly more complicated results.\n\n4. When first referred to, the _general_ form of this equation was\n  given (v. p. 29). The special form here assigned, in which\n  (h/sqrt{\u03c0}) is substituted for A, is commonly employed in\n  Probability, because the integral of y dx, between +infinity and\n  -infinity, becomes equal to unity. That is, the sum of all the\n  mutually exclusive possibilities is represented, as usual, by\n  unity. In this form of expression h is a quantity of the order\n  x^{-1}; for hx is to be a numerical quantity, standing as it does as\n  an index. The modulus, being the reciprocal of this, is of the same\n  order of quantities as the errors themselves. In fact, if we\n  multiply it by 0.4769... we have the so-called 'probable error.'\n\n5. See, for the explanation of this, and of the graphical method of\n  illustrating it, the note on p. 29.\n\n6. Broadly speaking, we may say that the above remarks hold good of\n  any law of frequency of error in which there are actual limits,\n  however wide, to the possible magnitude of an error. If there are no\n  limits to the possible errors, this characteristic of an average to\n  heap its results up towards the centre will depend upon\n  circumstances. When, as in the exponential curve, the approximation\n  to the base, as asymptote, is exceedingly rapid,--that is, when the\n  extreme errors are relatively very few,--it still holds good. But if\n  we were to take as our law of facility such an equation as\n  y = \u03c0/(1 + x^{2}), (as hinted by De Morgan and noted by Mr Edgeworth:\n  _Camb. Phil. Trans._ vol. X. p. 184, and vol. XIV. p. 160) it does\n  not hold good. The result of averaging is to _diminish_ the tendency\n  to cluster towards the centre.\n\n7. The reader will find the proofs of these and other similar formul\u00e6\n  in Galloway _on Probability_, and in Airy _on Errors_.\n\n8. The formula commonly used for the E.M.S. in this case is\n  (sum e^{2})/(n - 1) and not (sum e^{2})/n. The difference is trifling,\n  unless n be small; the justification has been offered for it that\n  since the sum of the squares measured from the true centre is a\n  minimum (that centre being the ultimate arithmetical mean) the sum\n  of the squares measured from the somewhat incorrectly assigned\n  centre will be somewhat larger.\n\n9. It appears to me that in strict logical propriety we should like to\n  know the probable error committed in _both_ the assignments of the\n  preceding two sections. But the profound mathematicians who have\n  discussed this question, and who alone are competent to treat it,\n  have mostly written with the practical wants of Astronomy in view;\n  and for this purpose it is sufficient to take account of the one\n  great desideratum, viz. the true values sought. Accordingly the only\n  rules commonly given refer to the probable error of the mean.\n\n10. i.e. as distinguished from acting upon them indirectly. This\n  latter proceeding, as explained in the chapter on Randomness, may\n  result in giving a non-uniform distribution.\n\n11. There is no difficulty in conceiving circumstances under which a\n  law very closely resembling this would prevail. Suppose, e.g., that\n  one of the two measurements had been made by a careful and skilled\n  mechanic, and the other by a man who to save himself trouble had put\n  in the estimate at random (within certain limits),--the firm having\n  a knowledge of this fact but being of course unable to assign the\n  two to their authors,--we should get very much such a Law of Error\n  as is supposed above.\n\n\n\n\nINDEX.\n\nAccidents 342\n\nAiry, G. B. 447, 484\n\nAnticipations, tacit 287\n\nArbuthnott 258\n\nAristotle 205, 307\n\nAverage\n  arithmetical 437\n  geometrical 439\n  median 442\n  consequences of 482\n  necessary results of 457\n  uses of 439, 489\n\nBabbage 343\n\nBags and balls 180, 411\n\nBelief\n  correctness of 125, 131, 178\n  gradations of 139\n  growth of 199\n  language of 143\n  measurement of 119, 125, 146\n  quantity of 133\n  test of 140, 149, 294\n  undue 129\n  vagueness of 127\n\nBentham 319, 323\n\nBernoulli 91, 117, 389\n\nBertillon 435\n\nBirths, male and female 90, 258, 263\n\nBoat race, Oxford and Cambridge 339\n\nBoole 183\n\nBuckle 237\n\nBuffon 153, 205, 352, 389\n\nBurgersdyck 311\n\nButler 209, 281, 333, 366\n\nCarlisle Tables 169\n\nCasual, meaning of 245\n\nCausation\n  need of 237\n  proof of 244\n\nCentre of gravity 467\n\nCertainty, in Law 324\n  reasonable 327\n  hypothetical 210\n\nChance\n  and Causation 244\n    Creation 258\n    Design 256\n    Genius 353\n  neglect of small 363\n  selections 338\n\nChauvenet 352\n\nClassification, numerical scheme of 48\n\nCoincidences 245\n\nCombinations and Permutations 87\n\nCommunism 375, 392\n\nConceptualism 275\n\nConflict of chances 418\n\nConsumptives, insurance of 227\n\nCournot 245, 255, 338\n\nCrackanthorpe 312, 320\n\nCraig, J. 192\n\nCrofton, M. W. 61, 101, 104\n\nDante 285\n\nDeflection\n  causes of 57\n  from aim 38\n\nDe Morgan 83, 106, 119, 122, 135, 177, 179, 197, 236, 247, 296, 308,\n350, 379, 382, 483\n\nDe Ros trial 255\n\nDigits, random 111, 114\n\nDiscontinuity 116\n\nDistribution, random 106\n\nDiagrams 29, 45, 118, 443, 476, 481, 493, 501\n\nDialectic 302, 320\n\nDonkin 123, 188, 283\n\nDuration of life 15, 441\n\nD\u00fcsing 259\n\nEbbinghaus 199\n\nEdgeworth, F. Y. 34, 119, 256, 339, 393, 435, 483\n\nEllis, L. 9\n\nEpidemics 62\n\nError, law of 29\n  asymmetrical 34, 441, 443\n  binomial 37, 457, 469, 480\n  geometrical 34, 502\n  heterogeneous 45\n  production of 36\n\nError\n  mean 446\n  probable 446, 472, 488\n  of mean square 447, 488\n\nEscapes, narrow 341\n\nExpectation, moral 388\n\nExperience and probability 74\n\nExponential curve 29\n\nExtraordinary\n  sense of 159, 423\n  stories 407, 421\n\nFallacies in Logic and Probability 367\n\nFatalism 243\n\nFechner 34, 389, 435, 441\n\nFluctuation 448\n  unlimited 73\n\nForbes, J. D. 188, 262\n\nFormal Logic 123\n\nFormal and Material treatment 86\n\nFree will 240\n\nGalloway 248, 448, 484\n\nGalton, F. 33, 50, 70, 318, 442, 451, 473, 502\n\nGambling\n  and Insurance 370\n  disadvantage of 384\n  final results of 385, 391\n\nGodfray, H. 99\n\nGrote, G. 307\n\nGuy 6\n\nHamilton, W. 266, 297\n\nHappiness, human 382\n\nHeads and Tails 77\n\nHeredity 50, 357\n\nHerschel 30, 466\n\nHoudin 361\n\nHume 236, 419, 433\n\nHypotheses 268\n\nImmediate inferences 121\n\nIndependent events 175, 246\n\nInduction\n  and Probability 194, 201, 208, 233, 358\n  difficulty of 213\n  pure 200\n\nInequality of wealth 382\n\nInference, rules of 167\n\nInoculation 374\n\nInsurance\n  justification of 149\n  difficulties of 221\n  life 151\n  peculiar case 224\n  theory of 372\n  varieties of 374\n\nInverse probability 179, 196, 249\n\nIrregularity, absolute and relative 6\n\nJacobs, J. 199\n\nJackson, J. G. 253\n\nJevons 37, 83, 136, 198, 201, 209, 247\n\nKant 310, 317\n\nKeckermann 298, 316\n\nKinds, natural 55\n\nKrug 324\n\nLambert 309\n\nLanguage of Chance 159\n\nLaplace 89, 120, 197, 237, 424\n\nLaw\n  absence of 101\n  empirical 160\n  of causation 206\n\nLeast squares 41, 467\n\nLeibnitz 309, 320\n\nLetters\n  lost 162, 368\n  misdirected 67, 237, 241\n\nLexis, W. 263, 441\n\nLimit\n  conception of 18, 109, 164\n  of possible fluctuation 32\n\nLines, random 113\n\nLister's method 187\n\nLotteries 128\n\nLunn, J. R. 248\n\nLikely, equally 77, 183\n\nMcAlister, D. 34, 187, 502\n\nMansel, H. L. 299, 301, 320\n\nMartingale 343\n\nMaterial and Formal Logic 265\n\nMaximum ordinate 441, 455\n\nMeasurement of\n  Belief 119\n  Memory 192\n\nMental qualities, measurement of 49\n\nMerriman, M. 352, 448, 460, 465\n\nMill, J. S. 131, 207, 266, 282, 402\n\nMilton, chance production of 353\n\nMiracles 428\n\nMichell, J. 260\n\nModality 295\n  divisions of 307\n  false 297\n  formal 298\n  in Law 319\n\nModulus 464, 472, 484\n\nMonro, C. J. 325, 416\n\nNames, reference of 270\n\nNations, comparison of 51\n\nNatural Kinds 55, 63, 71\n\nNecessary and impossible matter 310\n\nObjects and agencies 53\n\nOccam 314\n\nPaley 433\n\nPenny, tosses of 144\n\nPetrie, F. 498\n\nPetersburg Problem 19, 154\n\nPoisson 405\n\nPrantl 311\n\nPresumption, legal 329\n\nPr\u00e9vost 348\n\nProbability\n  definition of 165\n  relative 290\n  integral 463\n\nProbable\n  facts 269\n  value 441\n  error 446, 472\n\nProblem, Three point 104\n\nProctor, R. A. 262, 378\n\nProphecies, suicidal 226\n\nProvidence 89, 431\n\nPropositions, proportional 2\n\nPsychical research 256\n\nPyramid, the great 251\n\n\u03c0, digits in 111, 247\n\nQuartiles 446\n\nQuetelet 23, 30, 43, 91, 259, 330, 348, 454\n\nRandomness\n  etymology of 96\n  in firing 98\n  proof of 107\n\nRare events 349\n\nRealism 92\n\nReason, sufficient 82\n\nResiduals 460\n\nRoberts, C. 25\n\nRod\n  broken at random 98\n  thrown at random 103\n\nRules\n  Inductive and Deductive 176\n  of Succession 191\n  conflict of 222\n  plurality of 217\n\nSeries\n  definite proportions in 11\n  fixed and variable 16\n  ideal 95\n  peculiar 12\n\nShanks 248\n\nSkeat, W. W. 96\n\nSmiglecius 306, 316\n\nSmyth, P. 251\n\nSocialism 392\n\nSpiritualism 365\n\nStars, random arrangement of 108, 260\n\nStatistics\n  by Intercomparison 473\n  unconscious appeal to 400\n\nStatistical Journal 6\n\nStature\n  human 25, 471\n  French and English 44\n\nStephen, J. F. 282, 323, 326\n\nStewart, D. 209, 237\n\nSubjective and objective terms 160\n\nSuccession\n  long 360\n  Rule of 190, 362\n\nSuffield, G. 248\n\nSuicides 67, 237\n\nSurnames, extinction of 387\n\nSurprise, emotion of 157\n\nSyllogisms, pure and modal 316\n\nTaylor 329\n\nTestimony\n  single 411\n  combined 426\n  two kinds of 409\n  worthless 416\n\nThomson, W. 153, 314, 419\n\nTime\n  influence of 191\n  in Probability 279\n\nTodhunter 415\n\nTontines 380\n\nTriangle, random 103\n\nTucker, A. 127\n\nTypes\n  existence of 42, 60, 453\n  fixed and fluctuating 64, 93\n\nUeberweg 311\n\nUncertainty in life 370\n\nUniformity 240\n\nUnits of calculation 464\n\nVoluntary agency 65, 68, 85\n\nWatford 374\n\nWallis, J. 312\n\nWatson, H. W. 387\n\nWhately 297, 307\n\nWhist 401\n\nWhitworth, W. A. 87, 183, 384\n\nWilson, J. M. 104\n\nWitnesses, independent 405\n\nWolf 309\n\nWoolhouse 101\n\nCAMBRIDGE: PRINTED BY C.J. CLAY, M.A. AND SONS, AT THE UNIVERSITY PRESS.","title":"The Logic of Chance, 3rd edition: An Essay on the Foundations and Province of the Theory of Probability, With Especial Reference to Its Logical Bearings and Its Application to Moral and Social Science and to Statistics","tradition":"philosophy-ethics","translated_text":null,"word_count":169176}