Source: Henri Poincare, Science and Hypothesis, trans. W. J. G[reenstreet], with a preface by J. Larmor (London: Walter Scott Publishing, 1905), via the Internet Archive (scienceandhypoth00poinuoft) Source URL: https://archive.org/details/scienceandhypoth00poinuoft Translator: W. J. Greenstreet (1905) Public domain basis: Public-domain translation (1905), complete with Larmor's introduction. OCR text; some formulas are imperfect. IT is to be hoped that, as a consequence of the present active scrutiny of our educational aims and methods, and of the resulting encouragement of the study of modern languages, we shall not remain, as a nation, so much isolated from ideas and tendencies in continental thought and literature as we have been in the past. As things are, however, the translation of this book is doubtless required; at any rate, it brings vividly before us an instructive point of view. Though some of M. Poincare's chapters have been collected from well-known treatises written several years ago, and indeed are sometimes in detail not quite up to date, besides occasionally suggesting the suspicion that his views may possibly have been modified in the interval, yet their publication in a compact form has excited a warm welcome in this country. It must be confessed that the English language hardly lends itself as a perfect medium for the rendering of the delicate shades of suggestion and allusion characteristic of M. Poincare's play around his subject ; notwithstanding the excel lence of the translation, loss in this respect is inevitable. There has been of late a growing trend of opinion, prompted in part by general philosophical views, in the direction that the theoretical con structions of physical science are largely factitious, that instead of presenting a valid image of the relations of things on which further progress can be based, they are still little better than a mirage. The best method of abating this scepticism is to become acquainted with the real scope and modes of application of conceptions which, in the popular language of superficial exposition — and even in the unguarded and playful paradox of their authors, intended only for the instructed eye — often look bizarre enough. But much advantage will accrue if men of science become their own epistemologists, and show to the world by critical exposition in non-technical terms of the results and methods of their constructive work, that more than mere instinct is involved in it: the com munity has indeed a right to expect as much as this. It would be hard to find any one better qualified for this kind of exposition, either from the profundity of his own mathematical achievements, or from the extent and freshness of his interest in the theories of physical science, than the author of this book. If an appreciation might be ventured on as regards the later chapters, they are, perhaps, intended to present the stern logical analyst quizzing the cultivator of physical ideas as to what he is driving at, and wrhither he expects to go, rather than any responsible attempt towards a settled confession of faith. Thus, when M. Poincare allows himself for a moment to indulge in a process of evaporation of the Principle of Energy, he is content to sum up: " Eh bien, quelles que soient les notions nouvelles que les experiences futures nous donneront sur le monde, nous sommes surs d'avance qu'il y aura quelque chose qui demeurera constant et que nous pourrons appeler cncrgic" (p. 166), and to leave the matter there for his readers to think it out. Though hardly necessary in the original French, it may not now be superfluous to point out that independent reflection and criticism on the part of the reader are tacitly implied here as else where. An interesting passage is the one devoted to Maxwell's theory of the functions of the sether, and the comparison of the close-knit theories of the classical French mathematical physicists with the somewhat loosely-connected corpus of ideas by which Maxwell, the interpreter and successor of Faraday, has (posthumously) recast the whole face of physical science. How many times has that theory been re-written since Maxwell's day ? and yet how little has it been altered in essence, except by further developments in the problem of moving bodies, from the form in which he left it! If. as M. Poincare remarks, the French instinct for precision and lucid demonstration sometimes finds itself ill at ease with physical theories of the British school, he as readily admits (pp. 223, 224), and indeed fully appreciates, the advantages on the other side. Our owrn mental philosophers have been shocked at the point of view indicated by the proposition hazarded by Laplace, that a sufficiently developed intelligence, if it were made acquainted with the positions and motions of the atoms at any instant, could predict all future history: no amount of demur suffices sometimes to persuade them that this is not a conception universally entertained in physical science. It was not so even in Laplace's own day. From the point of view of the study of the evolution of the sciences, there are few episodes more instructive than the collision between Laplace and Young with regard to the theory of capil larity. The precise and intricate mathematical analysis of Laplace, starting from fixed pre conceptions regarding atomic forces which were to remain intact throughout the logical develop ment of the argument, came into contrast with the tentative, mobile intuitions of Young ; yet the latter was able to grasp, by sheer direct mental force, the fruitful though partial analogies of this recondite class of phenomena with more familiar operations of nature, and to form a direct picture of the way things interacted, such as could only have been illustrated, quite possibly damaged or obliterated, by premature effort to translate it into elaborate analytical formulas. The apcrgus of Young were apparently devoid of all cogency to Laplace; while Young expressed, doubtless in too extreme a way, his sense of the inanity of the array of mathematical logic of his rival. The subsequent history involved the Nemesis that the fabric of Laplace was taken down and recon structed in the next generation by Poisson; while the modern cultivator of the subject turns, at any rate in England, to neither of those expositions for illumination, but rather finds in the partial and succinct indications of Young the best start ing-point for further effort. It seems, however, hard to accept entirely the distinction suggested (p. 213) between the methods of cultivating theoretical physics in the two countries. To mention only two transcendent names which stand at the very front of two of the greatest developments of physical science of the last century, Carnot and Fresnel, their procedure was certainly not on the lines thus described. Possibly it is not devoid of significance that each of them attained his first effective recognition from the British school. It may, in fact, be maintained that the part played by mechanical and such-like theories — analogies if you will — is an essential one. The reader of this book will appreciate that the human mind -has need of many instruments of comparison and discovery besides the unrelenting logic of the infinitesimal calculus. The dynamical basis which underlies the objects of our most frequent ex perience has now been systematised into a great calculus of exact thought, and traces of new real relationships may come out more vividly when considered in terms of our familiar acquaintance with dynamical systems than when formulated under the paler shadow of more analytical abstractions. It is even possible for a constructive physicist to conduct his mental operations entirely by dynamical images, though Helmholtz, as well as our author, seems to class a predilection in this direction as a British trait. A time arrives when, as in other subjects, ideas have crystallised out into distinctness ; their exact verification and development then becomes a problem in mathe matical physics. But whether the mechanical analogies still survive, or new terms are now introduced devoid of all naive mechanical bias, it matters essentially little. The precise de termination of the relations of things in the rational scheme of nature in which we find ourselves is the fundamental task, and for its fulfilment in any direction advantage has to be taken of our knowledge, even when only partial, of new aspects and types of relationship which may have become familiar perhaps in quite different fields. Nor can it be forgotten that the most fruitful and fundamental conceptions of abstract pure mathematics itself have often been suggested from these mechanical ideas of flux and force, where the play of intuition is our most powerful guide. The study of the historical evolution of physical theories is essential to the complete understanding of their import. It is in b the mental workshop of a Fresnel, a Kelvin, or a Helmholtz, that profound ideas of the deep things of Nature are struck out and assume form; when pondered over and paraphrased by philosophers we see them react on the conduct of life : it is the business of criticism to polish them gradually to the common measure of human understanding. Oppressed though we are writh the necessity of being specialists, if we are to know anything thoroughly in these days of accumulated details, we may at any rate pro fitably study the historical evolution of knowledge over a field wider than our own. The aspect of the subject which has here been dwrelt on is that scientific progress, considered historically, is not a strictly logical process, and does not proceed by syllogisms. New ideas emerge dimly into intuition, come into con sciousness from nobody knows where, and become the material on which the mind operates, forging them gradually into consistent doctrine, which can be welded on to existing domains of know ledge. But this process is never complete : a crude connection can always be pointed to by a logician as an indication of the imperfection of human constructions. If intuition plays a part which is so important, it is surely necessary that we should possess a firm grasp of its limitations. In M. Poincare's earlier chapters the reader can gain very pleasantly a vivid idea of the various and highly complicated ways of docketing our perceptions of the relations of external things, all equally valid, that were open to the human race to develop. Strange to say, they never tried any of them ; and, satisfied with the very remarkable practical fitness of the scheme of geometry and dynamics that came naturally to hand, did not consciously trouble themselves about the possible existence of others until recently. Still more recently has it been found that the good Bishop Berkeley's logical jibes against the Newtonian ideas of fluxions and limiting ratios cannot be adequately appeased in the rigorous mathematical conscience, until our apparent continuities are resolved mentally into discrete aggregates which we only partially apprehend. The irresistible impulse to atomize everything thus proves to be not merely a disease of the physicist ; a deeper origin, in the nature of knowledge itself, is suggested. Everywhere want of absolute, exact adaptation can be detected, if pains are taken, between the various constructions that result from our mental activity and the impressions which give rise to them. The bluntness of our unaided sensual perceptions, which are the source in part of the intuitions of the race, is well brought out in this connection by M. Poincare. Is there real con tradiction ? Harmony usually proves to be re covered by shifting our attitude to the phenomena. All experience leads us to interpret the totality of things as a consistent cosmos — undergoing evolu tion, the naturalists will say — in the large-scale workings of which we are interested spectators and explorers, while of the inner relations and ramifications we only apprehend dim glimpses. When our formulation of experience is imperfect or even paradoxical, we learn to attribute the fault to our point of view, and to expect that future adaptation will put it right. But Truth resides in a deep well, and we shall never get to the bottom. Only, while deriving enjoyment and insight from M. Poincare's Socratic exposi tion of the limitations of the human outlook on the universe, let us beware of counting limitation as imperfection, and drifting into an inadequate conception of the wonderful fabric of human knowledge. J. LARMOR. AUTHOR'S PREFACE. To the superficial observer scientific truth is un assailable, the logic of science is infallible ; and if scientific men sometimes make mistakes, it is because they have not understood the rules of the game. Mathematical truths are derived from a few self-evident propositions, by a chain of flawless reasonings ; they are imposed not only on us, but on Nature itself. By them the Creator is fettered, as it were, and His choice is limited to a relatively small number of solutions. A few experiments, therefore, will be sufficient to enable us to determine what choice He has made. From each experiment a number of consequences will follow by a series of mathematical deductions, and in this way each of them will reveal to us a corner of the universe. This, to the minds of most people, and to students who are getting their first ideas of physics, is the origin of certainty in science. This is what they take to be the role of xxii AUTHOR'S PREFACE. experiment and mathematics. And thus, too, it was understood a hundred years ago by many men of science who dreamed of constructing the world with the aid of the smallest possible amount of material borrowed from experiment. But upon more mature reflection the position held by hypothesis was seen ; it was recognised that it is as necessary to the experimenter as it is to the mathematician. And then the doubt arose if all these constructions are built on solid foundations. The conclusion was drawn that a breath would bring them to the ground. This sceptical attitude does not escape the charge of superficiality. To doubt everything or to believe everything are two equally convenient solutions ; both dispense with the necessity of reflection. Instead of a summary condemnation we should . examine with the utmost care the role of hypo thesis ; we shall then recognise not only that it is necessary, but that in most cases it is legitimate. We shall also see that there are several kinds of hypotheses; that some are verifiable, and when once confirmed by experiment become truths of great fertility; that others may be useful to us in fixing our ideas; and finally, that others are hypotheses only in appearance, and reduce to definitions or to conventions in disguise. The AUTHOR'S PREFACE. xxiii latter are to be met with especially in mathematics , and in the sciences to which it is applied. From them, indeed, the sciences derive their rigour ; such conventions are the result of the unrestricted activity of the mind, which in this domain recog-/ nises no obstacle. For here the mind may affirms because it lays down its own la\vs ; but let us • clearly understand that while these laws are imposed on our science, which otherwise could not exist, they are not imposed on Nature. Are^; they then arbitrary? No; for if they were, they would not be fertile. Experience leaves us our freedom of choice, but it guides us by helping us to discern the most convenient path to follow. Our laws are therefore like those of an absolute monarch, who is wise and consults his council of state. Some people have been struck by this characteristic of free convention w^hich may be recognised in certain fundamental principles of the sciences. Some have set no limits to their generalisations, and at the same time they have forgotten that there is a difference between liberty and the purely arbitrary. So that they are com pelled to end in what is called nominalism; they have asked if the savant is not the dupe of his own definitions, and if the world he thinks he has discovered is not simply the creation of his own xxiv AUTHOR'S PREFACE. caprice.1 Under these conditions science would retain its certainty, but would not attain its object, and would become powerless. Now, we daily see what science is doing for us. This could not be unless it taught us something about reality; the aim of science is not things themselves, as the dogmatists in their simplicity imagine, but the relations between things; outside those relations there is no reality knowable. Such is the conclusion to which we are led; but to reach that conclusion we must pass in review the series of sciences from arithmetic and geometry to mechanics and experimental physics. What is the nature of mathematical reasoning ? Is it really deductive, as is commonly supposed ? Careful analysis shows us that it is nothing of the kind ; that it participates to some extent in the nature of inductive reasoning, and for that reason it is fruitful. But none the less does it retain its character of absolute rigour ; and this is what must first be shown. When we know more of this instrument which is placed in the hands of the investigator by mathematics, we have then to analyse another fundamental idea, that of mathematical magni- 1 Cf. M. le Roy: "Science et Philosophic," Revue de Afe/apkysique et de Morale ', 1901. AUTHOR'S PREFACE. tude. Do we find it in nature, or have we our selves introduced it ? And if the latter be the case, are we not running a risk of coming to incorrect conclusions all round ? Comparing the rough data of our senses with that extremely com plex and subtle conception \vhich mathematicians call magnitude, we are compelled to recognise a divergence. The framework into which \ve wish to make everything fit is one of our own construc tion ; but wre did not construct it at random, we constructed it by measurement so to speak; and that is \vhy wre can fit the facts into it without altering their essential qualities. Space is another framework which we impose on the world. Whence are the first principles of geometry derived ? Are they imposed on us by logic ? Lobatschewsky, by inventing non-Euclid ean geometries, has shown that this is not the case. Is space revealed to us by our senses ? No ; for the space revealed to us by our senses is absolutely different from the space of geometry. Is geometry derived from experience ? Careful discussion will give the answer — no ! We therefore conclude that the principles of geometry are only conventions ; but these conventions are not arbitrary, and if transported into another w;orld (w7hich I shall call the non-Euclidean world, and which I shall xxvi AUTHOR'S PREFACE. endeavour to describe), we shall find ourselves compelled to adopt more of them. In mechanics we shall be led to analogous con clusions, and we shall see that the principles of this science, although more directly based on experience, still share the conventional character of the geometrical postulates. So far, nominalism triumphs ; but we now come to the physical sciences, properly so called, and here the scene changes. We meet with hypotheses of another kind, and we fully grasp ho\v fruitful they are. No doubt at the outset theories seem unsound, and the history of science show's us how ephemeral they are ; but they do not entirely perish, and of each of them some traces still remain. It is these traces which we must try to discover, because in them and in them alone is the true reality. » ' The method of the physical sciences is based \upon the induction which leads us to expect the recurrence of a phenomenon when the circum stances which give rise to it are repeated. If all the circumstances could be simultaneously re produced, this principle could be fearlessly applied ; but this never happens; some of the circumstances will always be missing. Are we absolutely certain that they are unimportant ? Evidently not ! It may be probable, but it cannot be rigorously AUTHORS PREFACE. XXV11 certain. Hence the importance of the role that is played in the physical sciences by the law of probability. The calculus of probabilities is there fore not merely a recreation, or a guide to the baccarat player; and we must thoroughly examine the principles on which it is based. In this con nection I have but very incomplete results to lay before the reader, for the vague instinct wrhich enables us to determine probability almost defies analysis. After a study of the conditions under which the work of the physicist is carried on, I have thought it best to show him at work. For this purpose I have taken instances from the history of optics and of electricity. We shall thus see how the ideas of Fresnel and Maxwell took their rise, and what unconscious hypotheses were made by Ampere and the other founders of electro-dynamics. PART I. NUMBER AND MAGNITUDE, CHAPTER I. ON THE NATURE OF MATHEMATICAL REASONING, THE very possibility of mathematical science seems an insoluble contradiction. If this science is only deductive in appearance, from whence is derived that perfect rigour which is challenged by none? If, on the contrary, all the propositions which it enunciates may be derived in order by the rules of formal logic, how is it that mathematics is not reduced to a gigantic tautology? The syllo gism can teach us nothing essentially new, and if everything must spring from the principle of identity, then everything should be capable of being reduced to that principle. Are we then to admit that the enunciations of all the theorems with which so many volumes are filled, are only indirect ways of saying that A is A ? No doubt we may refer back to axioms which are at the source of all these reasonings. If it is felt that they cannot be reduced to the principle of contradiction, if we decline to see in them any more than experimental facts which have no part or lot in mathematical necessity, there is still one resource left to us: we may class them among a priori synthetic views. But this is no solution of the difficulty — it is merely giving it a name; and even if the nature of the synthetic views had no longer for us any mystery, the contradiction would not have disappeared ; it would have only been shirked. Syllogistic reasoning remains incapable of adding anything to the data that are given it ; the data are reduced to axioms, and that is all we should find in the conclusions. No theorem can be new unless a new axiom intervenes in its demonstration ; reasoning can only give us immediately evident truths borrowed from direct intuition; it would only be an inter mediary parasite. Should we not therefore have reason for asking if the syllogistic apparatus serves only to disguise what we have borrowed ? The contradiction will strike us the more if we open any book on mathematics; on every page the author announces his intention of generalising some proposition already known. Does the mathematical method proceed from the particular to the general, and, if so, how can it be called deductive ? NATURE OF MATHEMATICAL REASONING. 3 Finally, if the science of number were merely analytical, or could be analytically derived from a / few synthetic intuitions, it seems that a sufficiently / powerful mind could with a single glance perceive all its truths ; nay, one might even hope that some day a language would be invented simple enough for these truths to be made evident to any person of ordinary intelligence. Even if these consequences are challenged, it must be granted that mathematical reasoning has of itself a kind of creative virtue, and is therefore to be distinguished from the syllogism. The difference must be profound. We shall not, for instance, find the key to the mystery in the frequent use of the rule by which the same uniform operation applied to two equal numbers will give identical results. All these modes of reasoning, whether or not reducible to the syllogism, properly so called, retain the analytical character, and ipso facto, lose their power. The argument is an old one. Let us see how Leibnitz tried to show that two and two make four. I assume the number one to be defined, and also the operation A'+I — i.e., the adding of unity to a given number x. These definitions, whatever they may be, do not enter into the subsequent reasoning. I next define the numbers 2, 3, 4 by the equalities :— It cannot be denied that this reasoning is purely analytical. But if we ask a mathematician, he will reply: "This is not a demonstration properly so called; it is a verification." We have confined ourselves to bringing together one or other of two purely conventional definitions, and we have verified their identity ; nothing new has been learned. \Verification differs from proof precisely because it Is analytical, and because it leads to nothing. It leads to nothing because the conclusion is nothing but the premisses translated into another language. A real proof, on the other hand, is fruitful, because the conclusion is in a sense more general than the premisses. The equality 2 + 2 = 4 can be verified because it is particular. Each individual enuncia tion in mathematics may be always verified in the same way. But if mathematics could be reduced to a series of such verifications it would not be a science. A chess-player, for instance, does not create a science by winning a piece. There is no science but the science of the general. It may even be said that the object of the exact sciences is to dispense with these direct verifications. NATURE OF MATHEMATICAL REASONING. 5 Let us now see the geometer at work, and try to surprise some of his methods. The task is not without difficulty; it is not enough to open a book at random and to analyse any proof we may come across. First of all, geometry must be ex cluded, or the question becomes complicated by difficult problems relating to the role of the postulates, the nature and the origin of the idea of space. For analogous reasons we cannot avail ourselves of the infinitesimal calculus. We must seek mathematical thought where it has remained pure — i.e., in Arithmetic. But we still have to choose ; in the higher parts of the theory of numbers the primitive mathemati cal ideas have already undergone so profound an elaboration that it becomes difficult to analyse them. It is therefore at the beginning of Arithmetic that we must expect to find the explanation we seek ; but it happens that it is precisely in the proofs of the most elementary theorems that the authors of classic treatises have displayed the least precision and rigour. We may not impute this to them as a crime ; they have obeyed a necessity. Beginners are not prepared for real mathematical rigour ; they would see in it nothing but empty, tedious subtleties. It would be waste of time to try to make them more exacting ; they have to pass rapidly and without stopping over the road which was trodden slowly by the founders of the science. Why is so long a preparation necessary to habituate oneself to this perfect rigour, which it would seem should naturally be imposed on all minds ? This is a logical and psychological problem which is well worthy of study. But we shall not dwell on it ; it is foreign to our subject. All I wish to insist on is, that we shall fail in our purpose unless we reconstruct the proofs of the elementary theorems, and give them, not the rough form in which they are left so as not to weary the beginner, but the form which will satisfy the skilled geometer. DEFINITION OF ADDITION. I assume that the operation x+i has been denned; it consists in adding the number I to a given number x. Whatever may be said of this definition, it does not enter into the subsequent reasoning. We now have to define the operation x + a, which consists in adding the number a to any given number x. Suppose that we have defined the operation x+(a-i); the operation x + a will be defined by the equality : (i) x + a = [x + (a - i)] + i. We shall know what x + a is when we know what x+(a-i) is, and as I have assumed that to start with we know what x+i is, we can define successively and " by recurrence " the operations x + 2, x + 3, etc. This definition deserves a moment's NATURE OF MATHEMATICAL REASONING. 7 it is of a particular nature which distinguishes it even at this stage from the purely logical definition; the equality (i), in fact, contains an infinite number of distinct definitions, each having only one meaning when we know the meaning of its predecessor. PROPERTIES OF ADDITION. Associative. — I say that a-\-(b-\-c) = (a-\-b)-\-c; in fact, the theorem is true for c = i. It may then be written a-\-(b-\-i) = (a-{-b}-\-i; which, remembering the difference of notation, is nothing but the equality (i) by which I have just defined addition. Assume the theorem true for c=y, I say that it will be true for c = y+i. Let (a+b)+y=a+(b+y), it follows that i=[>+(& + y)]+i; or by def. (i)- (y + I)=a+(b + y + i)=a + [b+ (y + i)J , which shows by a series of purely analytical deduc tions that the theorem is true for y + i. Being true for c = i, we see that it is successively true for c = 2, c = 3, etc. Commutative. — (i) I say that a + i = i + a. The theorem is evidently true for a = i ; we can verify by purely analytical reasoning that if it is true for a --= y it will be true for a = y + i.1 Now, it is true for a=i, and therefore is true for a — 2, a = 3, and so on. This is what is meant by saying that the proof is demonstrated " by recurrence." (2) I say that a + b^b + a. The theorem has just been shown to hold good for b=i, and it may be verified analytically that if it is true for b=ft} it will be true for b=fi+i. The proposition is thus established by recurrence. DEFINITION OF MULTIPLICATION. We shall define multiplication by the equalities: (i) aXi=a. (2) axb=[ax(b-i)]+a. Both of these include an infinite number of definitions; having defined aXi, it enables us to define in succession aX2, aX3, and so on. PROPERTIES OF MULTIPLICATION. Distributive. — I say that (a-\-b)Xc = (aXc) + (bXc). We can verify analytically that the theorem is true for c = i; then if it is true for c = y, it will be true for c = y-\-i. The proposition is then proved by recurrence. Commutative. — (i) I say that aXi = iXa. The theorem is obvious for a = i. We can verify analytically that if it is true for a — a, it will be true for 5 constant in magnitude and direction. But this third rule is an experimental law. It is only approximately true: it is a bad definition. We are therefore reduced to Kirchoff's definition: force is the pro duct of the mass and the acceleration. This law of Newton in its turn ceases to be regarded as an experimental law, it is now only a definition. But as a definition it is insufficient, for we do not know what mass is. It enables us, no doubt, to calculate the ratio of two forces applied at different times to the same body, but it tells us nothing about the ratio of two forces applied to two different bodies. To fill up the gap we must have recourse to Newton's third law, the equality of action and reaction, still regarded not as an experimental law but as a definition. Two bodies, A and B, act on each other ; tvie accelera- THE CLASSICAL MECHANICS. IOT tion of A, multiplied by the mass of A, is equal to the action of B on A ; in the same way the acceleration of B, multiplied by the mass of B» is equal to the reaction of A on B. As, by definition, the action and the reaction are equal, the masses of A and B arc respectively in the inverse ratio of their masses. Thus is the ratio of the two masses defined, and it is for experiment to verify that the ratio is constant. This would do very well if the two bodies were alone and could be abstracted from the action of the rest of the world ; but this is by no means the case. The acceleration of A is not solely due to the action of B, but to that of a multitude of. -' other bodies, C, D, . . . To apply the preceding rule we must decompose the acceleration of A into many components, and find out which of these components is due to the action of B. The decomposition would still be possible if we suppose that the action of C on A is simply added to that of B on A, and that the presence of the body C does not in any way modify the action of B on A, or that the presence of B does not modify the action of C on A ; that is, if we admit that any two bodies attract each other, that their mutual action is along their join, and is only de pendent on their distance apart ; if, in a word, we admit the hypothesis of central forces. We know that to determine the masses of the heavenly bodies we adopt quite a different prin ciple. The law of gravitation teaches us that the attraction of two bodies is proportional to their masses; if r is their distance apart, m and ni their masses, k a constant, then their attraction will be knun'/r2. What we are measuring is therefore not mass, the ratio of the force to the acceleration, but the attracting mass ; not the inertia of the body, but its attracting power. It is an indirect process, the use of which is not indispensable theoretically. We might have said that the attraction is in versely proportional to the square of the distance, without being proportional to the product of the masses, that it is equal to //r2 and not to kinm'. If it were so, we should nevertheless, by observing the relative motion of the celestial bodies, be able to calculate the masses of these bodies. But have we any right to admit the hypothesis of central forces ? Is this hypothesis rigorously accurate ? Is it certain that it will never be falsified by experiment ? Who will venture to make such an assertion ? And if we must abandon this hypothesis, the building which has been so laboriously erected must fall to the ground. We have no longer any right to speak of the component of the acceleration of A which is due to the action of B. We have no means of distinguishing it from that which is due to the action of C or of any other body. The rule becomes inapplicable in the measurement of masses. What then is left of the principle of the equality of action and reaction ? If we reject the hypothesis of central forces this prin- THE CLASSICAL MECHANICS. 103 ciple must go too ; the geometrical resultant of all the forces applied to the different bodies of a system abstracted from all external action will be zero. In other words, the motion of the centre of gravity of this system will be uniform and in a straight line. Here would seem to be a means of defining mass. The position of the centre of gravity evidently depends on the values given to the masses ; we must select these values so that the motion of the centre of gravity is uniform and rectilinear. This will always be possible if Newton's third law holds good, and it will be in general possible only in one way. But no system exists which is abstracted from all external action; every part of the universe is subject, more or less, to the action of the other parts. The law of the Motion of the centre of gravity is only rigorously true when applied to the whole universe. But then, to obtain the values of the masses we must find the motion of the centre of gravity of the universe. The absurdity of this conclusion is obvious ; the motion of the centre of gravity of the universe will be for ever to us unknown. Nothing, therefore, is left, and our efforts are fruitless. There is no escape from the following definition, which is only a confession of failure : Masses are co-efficients which it is found convenient to introduce into calculations. We could reconstruct our mechanics by giving to our masses different values. The new me chanics would be in contradiction neither with experiment nor with the general principles of dynamics (the principle of inertia, proportion ality of masses and accelerations, equality of action and reaction, uniform motion of the centre of gravity in a straight line, and areas). But the equations of this mechanics would not be so simple. Let us clearly understand this. It would be only the first terms which would be less simple — i.e., those we already know through experiment ; perhaps the small masses could be slightly altered without the complete equations gaining or losing in simplicity. Hertz has inquired if the principles of mechanics are rigorously true. " In the opinion of many physicists it seems inconceivable that experiment will ever alter the impregnable principles of mechanics; and yet, what is due to experiment may always be rectified by experiment." From what we have just seen these fears would appear to be groundless. The principles of dynamics appeared to us first as experimental truths, but we have been compelled to use them as defini tions. It is by definition that force is equal to the product of the mass and the acceleration ; this is a principle which is henceforth beyond the reach of any future experiment. Thus it is by definition that action and reaction are equal and opposite. But then it will be said, these unverifiable principles are absolutely devoid of any significance. They cannot be disproved by experiment, but we can learn from them nothing THE CLASSICAL MECHANICS. 105 of any use to us ; \vhat then is the use of studying dynamics ? This somewhat rapid condemnation would be rather unfair. There is not in Nature any system perfectly isolated, perfectly abstracted from all external action ; but there are systems which are nearly isolated. If we observe such a system, we can study not only the relative motion of its different parts writh respect to each other, but the motion of its centre of gravity with respect to the other parts of the universe. We then find that the motion of its centre of gravity is nearly uniform and rectilinear in conformity with Newton's Third Law. This is an experimental fact, which cannot be invalidated by a more accurate experiment. What, in fact, would a more accurate experiment teach us ? It \vould teach us that the law is only approximately true, and we know that already. Thus is explained how experiment may serve as a basis for the principles of mechanics, and yet will never invalidate them. Anthropomorphic Mechanics. — It will be said that Kirchoff has only followed the general tendency of mathematicians towards nominalism ; from this his skill as a physicist has not saved him. He wanted a definition of a force, and he took the first that came handy ; but we do not require a definition of force ; the idea of force is primitive, irreducible, indefinable ; we all know what it is ; of it we have direct intuition. This direct intuition arises from the idea of effort which is familiar to us from childhood. But in the first place, even if this direct intuition made known to us the real nature of force in itself, it would prove to be an insufficient basis for mechanics ; it would, moreover, be quite useless. The important thing is not to know what force is, but how to measure it. Everything which does not teach us how to measure it is as useless to the mechanician as, for instance, the subjective idea of heat and cold to the student of heat. This subjective idea cannot be translated into numbers, and is therefore useless ; a scientist whose skin is an absolutely bad conductor of heat, and who, therefore, has never felt the sensation of heat or cold, would read a thermometer in just the same way as any one else, and would have enough material to construct the whole of the theory of heat. Now this immediate notion of effort is of no use to us in the measurement of force. It is clear, for example, that I shall experience more fatigue in lifting a weight of 100 Ib. than a man who is accustomed to lifting heavy burdens. But there is more than this. This notion of effort does not teach us the nature of force ; it is definitively re duced to a recollection of muscular sensations, and no one will maintain that the sun experiences a muscular sensation when it attracts the earth. All that we can expect to find from it is a symbol, less precise and less convenient than the arrows (to denote direction) used by geometers, and quite as remote from reality. Anthropomorphism plays a considerable historic THE CLASSICAL MECHANICS. 107 role ill the genesis of mechanics ; perhaps it may yet furnish us with a symbol which some minds may find convenient; but it can be the foundation of nothing of a really scientific or philosophical character. The Thread School. — M. Andrade, in his Lccons de Mecanique physique, has modernised anthropo morphic mechanics. To the school of mechanics with which Kirchoff is identified, he opposes a school which is quaintly called the " Thread School." This school tries to reduce everything to the con sideration of certain material systems of negligible mass, regarded in a state of tension and capable of transmitting considerable effort to distant bodies — systems of which the ideal type is the fine string, wire, or thread. A thread which transmits any force is slightly lengthened in the direction of that force; the direction of the thread tells us the direction of the force, and the magni tude of the force is measured by the lengthening of the thread. We may imagine such an experiment as the following : — A body A is attached to a thread ; at the other extremity of the thread acts a force which is made to vary until the length of the thread is increased by a, and the acceleration of the body A is recorded. A is then detached, and a body B is attached to the same thread, and the same or another force is made to act until the increment of length again is a, and the acceleration of B is noted. The experiment is then renewed with both A and B until the incre ment of length is ft. The four accelerations observed should be proportional. Here we have an experimental verification of the law of accelera tion enunciated above. Again, we may consider a body under the action of several threads in equal tension, and by experiment we determine the direction of those threads when the body is in equilibrium. This is an experimental verification of the law of the composition of forces. But, as a matter of fact, what have we done ? We have defined the force acting on the string by the deformation of the thread, which is reasonable enough; we have then assumed that if a body is attached to this thread, the effort which is transmitted to it by the thread is equal to the action exercised by the body on the thread ; in fact, we have used the principle of action and reaction by considering it, not as an experimental truth, but as the very definition of force. This definition is quite as conventional as that of Kirchoff, but it is much less general. All the forces are not transmitted by the thread (and to compare them they would all have to be transmitted by identical threads). If we even admitted that the earth is attached to the sun by an invisible thread, at any rate it will be agreed that we have no means of measuring the increment of the thread. Nine times out of ten, in con sequence, our definition will be in default ; no THE CLASSICAL MECHANICS. IOQ sense of any kind can be attached to it, and we must fall back on that of Kirchoff. Why then go on in this roundabout way ? You admit a certain definition of force which has a meaning only in certain particular cases. In those cases you verify by experiment that it leads to the law of accelera tion. On the strength of these experiments you then take the law of acceleration as a definition of force in all the other cases. Would it not be simpler to consider the law of acceleration as a definition in all cases, and to regard the experiments in question, not as verifica tions of that law, but as verifications of the principle of action and reaction, or as proving the deformations of an elastic body depend only on the forces acting on that body ? Without taking into account the fact that the conditions in which your definition could be accepted can only be very imperfectly fulfilled, that a thread is never without mass, that it is never isolated from all other forces than the reaction of the bodies attached to its extremities. The ideas expounded by M. Andrade are none the less very interesting. If they do not satisfy our logical requirements, they give us a better view of the historical genesis of the fundamental ideas of mechanics. The reflections they suggest show us how the human mind passed from a naive anthropomorphism to the present conception of science. We see that we end with an experiment which is very particular, and as a matter of fact very crude, and we start with a perfectly general law, perfectly precise, the truth of which we regard as absolute. We have, so to speak, freely conferred this certainty on it by looking upon it as a con vention. Are the laws of acceleration and of the com position of forces only arbitrary conventions ? Conventions, yes; arbitrary, no — they would be so if we lost sight of the experiments which led the founders of the science to adopt them, and which, imperfect as they were, were sufficient to justify their adoption. It is well from time to time to let our attention dwell on the experimental origin of these conventions. CHAPTER VII. RELATIVE AND ABSOLUTE MOTION. The Principle of Relative Motion. — Sometimes endeavours have been made to connect the law of acceleration with a more general principle. The movement of any system whatever ought to obey the same laws, whether it is referred to fixed axes or to the movable axes which are implied in uniform motion in a straight line. This is the principle of relative motion ; it is imposed upon us for two reasons: the commonest experi ment confirms it; the consideration of the contrary hypothesis is singularly repugnant to the mind. Let us admit it then, and consider a body under the action of a force. The relative motion of this body with respect to an observer moving with a uniform velocity equal to the initial velocity of the body, should be identical with what would be its absolute motion if it started from rest. We con clude that its acceleration must not depend upon its absolute velocity, and from that we attempt to deduce the complete law of acceleration. For a long time there have been traces of this proof in the regulations for the degree of IB. es Sc. It is clear that the attempt has failed. The obstacle which prevented us from proving the law of acceleration is that we have no definition of force. This obstacle subsists in its entirety, since the principle invoked has not furnished us wdth the missing definition. The principle of relative motion is none the less very interesting, and deserves to be considered for its own sake. Let us try to enunciate it in an accurate manner. We have said above that the accelerations of the different bodies which form part of an isolated system only depend on their velocities and their relative positions, and not on their velocities and their absolute positions, provided that the mov able axes to which the relative motion is referred move uniformly in a straight line; or, if it is pre ferred, their accelerations depend only on the differences of their velocities and the differences of their co-ordinates, and not on the absolute values of these velocities and co-ordinates. If this prin ciple is true for relative accelerations, or rather for differences of acceleration, by combining it with the law of reaction we shall deduce that it is true for absolute accelerations. It remains to be seen how we can prove that differences of accelera tion depend only on differences of velocities and co-ordinates; or, to speak in mathematical language, that these differences of co-ordinates satisfy differential equations of the second order. Can this proof be deduced from experiment or from a priori conditions? Remembering what we RELATIVE AND ABSOLUTE MOTION. 113 have said before, the reader will give his own answer. Thus enunciated, in fact, the principle of relative motion curiously resembles what I called above the generalised principle of inertia; it is not quite the same thing, since it is a question of differences of co-ordinates, and not of the co ordinates themselves. The new principle teaches us something more than the old, but the same discussion applies to it, and would lead to the same conclusions. We need not recur to it. Newton's Argument. — Here we find a very im portant and even slightly disturbing question. I have said that the principle of relative motion was not for us simply a result of experiment; and that a priori every contrary hypothesis would be repugnant to the mind. But, then, why is the principle only true if the motion of the movable axes is uniform and in a straight line? It seems that it should be imposed upon us with the same force if the motion is accelerated, or at any rate if it reduces to a uniform rotation. In these two cases, in fact, the principle is not true. I need not dwell on the case in which the motion of the axes is in a straight line and not uniform. The paradox does not bear a moment's examination. If I am in a railway carriage, and if the train, striking against any obstacle whatever, is suddenly stopped, I shall be projected on to the opposite side, although I have not been directly acted upon by any force. There is nothing mysterious in that, and if I have not been subject to the action of any external force, the train has experienced an external impact. There can be nothing para doxical in the relative motion of two bodies being disturbed when the motion of one or the other is modified by an external cause. Nor need I dwell on the case of relative motion referring to axes which rotate uniformly. If the sky were for ever covered with clouds, and if we had no means of observing the stars, we might, nevertheless, con clude that the earth turns round. We should be warned of this fact by the flattening at the poles, or by the experiment of Foucault's pendulum. And yet, would there in this case be any meaning in saying that the earth turns round ? If there is I no absolute space, can a thing turn without turn ing with respect to something; and, on the other hand, how can we admit Newton's conclusion and believe in absolute space? But it is not sufficient to state that all possible solutions are equally unpleasant to us. We must analyse in each case the reason of our dislike, in order to make our choice with the knowledge of the cause. The long discussion which follows must, therefore, be excused. Let us resume our imaginary story. Thick clouds hide the stars from men who cannot observe them, and even are ignorant of their existence. How will those men know that the earth turns round ? No doubt, for a longer period than did our ancestors, they will regard the soil on which they stand as fixed and immovable! They will RELATIVE AND ABSOLUTE MOTION. 1 15 wait a much longer time than we did for the coming of a Copernicus; but this Copernicus will come at last. How will he come? In the first place, the mechanical school of this world would not run their heads against an absolute contradic tion. In the theory of relative motion we observe, besides real forces, t\vo imaginary forces, which we call ordinary centrifugal force and compounded centrifugal force. Our imaginary scientists can thus explain everything by looking upon these two forces as real, and they would not see in this a contradiction of the generalised principle of inertia, for these forces would depend, the one on the relative positions of the different parts of the system, such as real attractions, and the other on their relative velocities, as in the case of real frictions. Many difficulties, however, would before long awaken their attention. If they succeeded in realising an isolated system, the centre of gravity of this system would not have an approximately rectilinear path. They could invoke, to explain this fact, the centrifugal forces which they would regard as real, and which, no doubt, they would attribute to the mutual actions of the bodies — only they would not see these forces vanish at great distances— that is to say, in proportion as the isolation is better realised. Far from it. Centri fugal force increases indefinitely with distance. Already this difficulty would seem to them suffi ciently serious, but it would not detain them for long. They would soon imagine some very subtle medium analogous to our ether, in which all bodies would be bathed, and which would exer cise on them a repulsive action. But that is not all. Space is symmetrical — yet the laws of motion would present no symmetry. They should be able to distinguish between right and left. They would see, for instance, that cyclones always turn in the same direction, while for reasons of symmetry they should turn indifferently in any direction. If our scientists were able by dint of much hard work to make their universe perfectly symmetrical, this symmetry would not subsist, although there is no apparent reason why it should be disturbed in one direction more than in another. They would extract this from the situation no doubt — they would invent something which would not be more extraordinary than the glass spheres of Ptolemy, and would thus go on accumulating complications until the long-ex pected Copernicus would sweep them all away with a single blow, saying it is much more simple to admit that the earth turns round. Just as our Copernicus said to us: " It is more convenient to suppose that the earth turns round, because the laws of astronomy are thus expressed in a more simple language," so he would say to them: "It is more convenient to suppose that the earth turns round, because the laws of mechanics are thus expressed in much more simple language. That does not prevent absolute space — that is to say, the point to which we must refer the earth to RELATIVE AND ABSOLUTE MOTION. 117 know if it really does turn round — from having no objective existence. And hence this affirma tion: "the earth turns round," has no meaning, since it cannot be verified by experiment; since such an experiment not only cannot be realised or even dreamed of by the most daring Jules Verne, but cannot even be conceived of without con tradiction ; or, in other words, these two proposi tions, "the earth turns round," and, "it is morel convenient to suppose that the earth turns round," | have one and the same meaning. There is nothing more in one than in the other. Perhaps they will not be content with this, and may find it surpris ing that among all the hypotheses, or rather all the conventions, that can be made on this subject there is one which is more convenient than the rest? But if we have admitted it without diffi culty when it is a question of the laws of astronomy, why should we object when it is a question of the laws of mechanics ? We have seen that the co-ordinates of bodies are deter mined by differential equations of the second order, and that so are the differences of these co-ordinates. This is what we have called the generalised principle of inertia, and the principle of relative motion. If the distances of these bodies were determined in the same way by equations of the second order, it seems that the mind should be entirely satisfied. How far does the mind receive this satisfaction, and why is it not content with it ? To explain this we had better take a simple example. I assume a system analogous to our solar system, but in which fixed stars foreign to this system cannot be perceived, so that astronomers can only observe the mutual distances of planets and the sun, and not the absolute longitudes of the planets. If we deduce directly from Newton's law the differential equa tions which define the variation of these distances, these equations will not be of the second order. I mean that if, outside Newton's law, we knew the initial values of these distances and of their de rivatives with respect to time — that would not be sufficient to determine the values of these same distances at an ulterior moment. A datum would be still lacking, and this datum might be, for example, what astronomers call the area-constant. But here \ve may look at it from two different points of view. We may consider two kinds of constants. In the eyes of the physicist the world reduces to a series of phenomena depending, on the I one hand, solely on initial phenomena, and, on the other hand, on the laws connecting consequence |and antecedent. If observation then teaches us that a certain quantity is a constant, we shall have a choice of two ways of looking at it. So let us admit that there is a law which requires that this quantity shall not vary, but that by chance it has been found to have had in the beginning of time this value rather than that, a value that it has kept ever since. This quantity might then be called an accidental constant. Or again, let us RELATIVE AND ABSOLUTE MOTION. Il<) admit on the contrary that there is a law of nature which imposes on this quantity this value and not that. We shall then have what may be called an essential constant. For example, in virtue of the laws of Newton the duration of the revolution of the earth must be constant, But if it is 366 and something sidereal days, and not 300 or 400, it is because of some initial chance or other. It is an accidental constant. If, on the other hand, the exponent of the distance which figures in the expression of the attractive force is equal to -2 and not to -3, it is not by chance, but because it is required by Newton's la\v. It is an essential constant. I do not know if this manner of giving to chance its share is legitimate in itself, and if there is not some artificiality about this distinc tion; but it is certain at least that in proportion as Nature has secrets, she will be strictly arbitrary and always uncertain in their application. As far as the area-constant is concerned, we are accus tomed to look upon it as accidental. Is it certain that our imaginary astronomers would do the same ? If they were able to compare two different solar systems, they would get the idea that this constant may assume several different values. But I supposed at the outset, as I was entitled to do, that their system would appear isolated, and that they would see no star which was foreign to their system. Under these conditions they could only detect a single constant, which would have an absolutely invariable, unique value. They would be led no doubt to look upon it as an essential constant. One word in passing to forestall an objection. The inhabitants of this imaginary world could neither observe nor define the area-constant as we do, because absolute longitudes escape their notice; but that would not prevent them from being rapidly led to remark a certain constant which would be naturally introduced into their equations, and which would be nothing but what we call the area-constant. But then what would happen ? If the area-constant is regarded as essential, as dependent upon a law of nature, then in order to calculate the distances of the planets at any given moment it would be sufficient to know the initial values of these distances and those of their first derivatives. From this new point of view, dis tances will be determined by differential equations of the second order. Would this completely satisfy the minds of these astronomers ? I think not. In the first place, they wTould very soon see that in differentiating their equations so as to raise them to a higher order, these equations would become much more simple, and they would be especially struck by the difficulty which arises from symmetry. They would have to admit different laws, according as the aggregate of the planets presented the figure of a certain polyhedron or rather of a regular polyhedron, and these conse quences can only be escaped by regarding the areaconstant as accidental. I have taken this particular RELATIVE AND ABSOLUTE MOTION. 121 example, because I have imagined astronomers who would not be in the least concerned with terrestrial mechanics and whose vision would be bounded by the solar system. But our con clusions apply in all cases. Our universe is more extended than theirs, since we have fixed stars; but it, too, is very limited, so we might reason on the whole of our universe just as these astronomers do on their solar system. We thus see that we should be definitively led to conclude that the equations which define distances are of an order higher than the second. Why should this alarm us — why do we find it perfectly natural that the sequence of phenomena depends on initial values of the first derivatives of these distances, while we hesitate to admit that they may depend on the initial values of the second derivatives ? It can only be because of mental habits created in us by the constant study of the generalised principle of inertia and of its consequences. The values of the distances at any given moment depend upon their initial values, on that of their first derivatives, and something else. What is that something else ? If we do not want it to be merely one of the second derivatives, we have only the choice of hypotheses. Suppose, as is usually done, that this something else is the absolute orientation of the universe in space, or the rapidity with which this orientation varies; this may be, it certainly is, the most con venient solution for the geometer. But it is not the most satisfactory for the philosopher, because this orientation does not exist. We may assume that this something else is the position or the velocity of some invisible body, and this is what is done by certain persons, who have even called the body Alpha, although we are destined to never know anything about this body except its name. This is an artifice entirely analogous to that of which I spoke at the end of the paragraph con taining my reflections on the principle of inertia. But as a matter of fact the difficulty is artificial. Provided that the future indications of our instru ments can only depend on the indications which they have given us, or that they might have formerly given us, such is all we want, and with these conditions we may rest satisfied. CHAPTER VIII. ENERGY AND THERMODYNAMICS. Energetics. — The difficulties raised by the classi cal mechanics have led certain minds to prefer a new system which they call Energetics. Energetics took its rise in consequence of the discovery of the principle of the conservation of energy. Helmholtz gave it its definite form. We begin by de fining two quantities which play a fundamental part in this theory. They are kinetic energy, or vis viva, and potential energy. Every change that the bodies of nature can undergo is regulated by two experimental laws. First, the sum of the kinetic and potential energies is constant. This is the principle of the conservation of energy. Second, if a system of bodies is at A at the time t0, and at B at the time £15 it always passes from the first position to the second by such a path that the mean value of the difference between the two kinds of energy in the interval of time which separates the two epochs t0 and tl is a minimum. This is Hamilton's principle, and is one of the forms of the principle of least action. The energetic theory has the following advantages over the classical. First, it is less incomplete — that is to say, the principles of the conservation of energy and of Hamilton teach us more than the fundamental principles of the classical theory, and exclude certain motions which do not occur in nature and which would be compatible with the classical theory. Second, it frees us from the hypothesis of atoms, which it was almost impos sible to avoid with the classical theory. But in its turn it raises fresh difficulties. The definitions of the two kinds of energy would raise difficulties almost as great as those of force and mass in the first system. However, we can get out of these difficulties more easily, at any rate in the simplest cases. Assume an isolated system formed of a certain number of material points. Assume that these points are acted upon by forces depending only on their relative position and their dis tances apart, and independent of their velocities. In virtue of the principle of the conservation of energy there must be a function of forces. In this simple case the enunciation of the principle of the conservation of energy is of extreme simplicity. A certain quantity, which may be determined by experiment, must remain constant. This quantity is the sum of two terms. The first depends only on the position of the material points, and is inde pendent of their velocities; the second is pro portional to the squares of these velocities. This decomposition can only take place in one way. The first of these terms, which I shall call U, will ENERGY AND THERMO-DYNAMICS. 125 be potential energy ; the second, which I shall call T, will be kinetic energy. It is true that if T + U is constant, so is any function of T + U, <£ (T + U). But this function (T+U) will not be the sum of two terms, the one independent of the velocities, and the other proportional to the square of the velocities. Among the functions which remain constant there is only one which enjoys this pro perty. It is T + U (or a linear function of T + U), it matters not which, since this linear function may always be reduced to T + U by a change of unit and of origin. This, then, is what we call energy. The first term we shall call potential energy, and the second kinetic energy. The definition of the two kinds of energy may therefore be carried through without any ambiguity. So it is with the definition of mass. Kinetic energy, or vis viva, is expressed very simply by the aid of the masses, and of the relative velocities of all the material points with reference to one of them. These relative velocities may be observed, and when we have the expression of the kinetic energy as a function of these relative velocities, the co efficients of this expression will give us the masses. So in this simple case the fundamental ideas can be defined without difficulty. But the difficulties reappear in the more complicated cases if the forces, instead of depending solely on the dis tances, depend also on the velocities. For ex ample, Weber supposes the mutual action of two electric molecules to depend not only on their distance but on their velocity and on their accelera tion. If material points attracted each other according to an analogous law, U would depend on the velocity, and it might contain a term proportional to the square of the velocity. How can we detect among such terms those that arise from T or U ? and how, therefore, can we dis tinguish the two parts of the energy ? But there is more than this. How can we define energy itself? We have no more reason to take as our definition T+U rather than any other function of T + U, when the property which characterised T + U has disappeared — namely, that of being the sum of two terms of a particular form. But that is not all. We must take account, not only of mechanical energy properly so called, but of the other forms of energy— heat, chemical energy, electrical energy, etc. The principle of the con servation of energy must be written T+U+Q= a constant, where T is the sensible kinetic energy, U the potential energy of position, depending only on the position of the bodies, Q the internal molecular energy under the thermal, chemical, or electrical form. This would be all right if the three terms were absolutely distinct ; if T were proportional to the square of the velocities, U independent of these velocities and of the state of the bodies, Q independent of the velocities and of the positions of the bodies, and depending only on their internal state. The expression for the energy could be decomposed in one way only into three ENERGY AND THERMO-DYNAMICS. 127 terms of this form. But this is not the case. Let us consider electrified bodies. The electro-static energy due to their mutual action will evidently depend on their charge — i.e., on their state ; but it will equally depend on their position. If these bodies are in motion, they will act electro-dynamically on one another, and the electro-dynamic energy will depend not only on their state and their position but on their velocities. We have therefore no means of making the selec tion of the terms which should form part of T, and U, and Q, and of separating the three parts of the energy. IfT + U + Q is constant, the same is true of any function whatever, (T + U + Q). If T + U + Q were of the particular form that I have suggested above, no ambiguity would ensue. Among the functions (T + U + Q) which remain constant, there is only one that would be of this particular form, namely the one which I would agree to call energy. But I have said this is not rigorously the case. Among the functions that remain constant there is not one which can rigorously be placed in this particular form. How then can we choose from among them that which should be called energy ? We have no longer any guide in our choice. Of the principle of the conservation of energy there is nothing left then but an enunciation:— There is something which remains constant. In this form it, in its turn, is outside the bounds of ex periment and reduced to a kind of tautology. It is clear that if the world is governed by laws there will be quantities which remain constant. Like Newton's laws, and for an analogous reason, the principle of the conservation of energy being based on experiment, can no longer be invalidated by it. This discussion shows that, in passing from the classical system to the energetic, an advance has been made ; but it shows, at the same time, that we have not advanced far enough. Another objection seems to be still more serious. The principle of least action is applicable to revers ible phenomena, but it is by no means satisfactory as far as irreversible phenomena are concerned. Helmholtz attempted to extend it to this class of phenomena, but he did not and could not succeed. So far as this is concerned all has yet to be done. The very enunciation of the principle of least action is objectionable. To move from one point to another, a material molecule, acted upon by no force, but compelled to move on a surface, will take as its path the geodesic line — i.e., the shortest path. This molecule seems to know the point to which we want to take it, to foresee the time that it will take it to reach it by such a path, and then to know how to choose the most convenient path. The enunciation of the prin ciple presents it to us, so to speak, as a living and free entity. It is clear that it would be better to replace it by a less objectionable enunciation, one in which, as philosophers would say, final ENERGY AND THERMODYNAMICS, I2Q effects do not seem to be substituted for acting causes. Thcr mo-dynamics. — The role of the two funda mental principles of thermo-dynamics becomes daily more important in all branches of natural philosophy. Abandoning the ambitious theories of forty years ago, encumbered as they were with molecular hypotheses, we now try to rest on thermo-dynamics alone the entire edifice of mathematical physics. Will the two principles of Mayer and of Clausius assure to it founda tions solid enough to last for some time ? We all feel it, but whence does our confidence arise ? An eminent physicist said to me one day, apropos of the law of errors: — every one stoutly \ believes it, because mathematicians imagine that it is an effect of observation, and observers imagine that it is a mathematical theorem. And this was for a long time the case with the principle of the conservation of energy. It is no longer the same now. There is no one who does not know that it is an experimental fact. But then who gives us the right of attributing to the principle itself more generality and more precision than to the experi ments which have served to demonstrate it? This is asking, if it is legitimate to generalise, as we do every day, empiric data, and I shall not be so foolhardy as to discuss this question, after so many philosophers have vainly tried to solve it. One thing alone is certain. If this permission were refused to us, science could not exist; or at least would be reduced to a kind of inventory, to the ascertaining of isolated facts. It would not longer be to us of any value, since it could not satisfy our need of order and harmony, and because it would be at the same time incapable of prediction.. As the circumstances which have preceded any fact whatever will never again, in all probability, be simultaneously reproduced, we already require a first generalisation to predict whether the fact will be renewed as soon as the least of these circum stances is changed, f But every proposition may be generalised in an infinite number of ways. Among all possible generalisations we must choose, and we cannot but choose the simplest. We are therefore led to adopt the same course as if a simple law were, other things being equal, more probable than a complex law. A century ago it was frankly confessed and proclaimed abroad that Nature loves simplicity; but Nature has proved the contrary since then on more than one occasion. We no longer confess this tendency, and we only keep of it what is indispensable, so that science may not become impossible. In formulating a general, simple, and formal law, based on a comparatively small number of not alto gether consistent experiments, we have only obeyed a necessity from which the human mind cannot free itself. ^But there is something more, and that is why I dwell on this topic. No one doubts that Mayer's principle is not called upon to survive all the particular laws from which it was deduced, in ENERGY AND THERMO-DYNAMICS. 131 the same way that Newton's law has survived the laws of Kepler from which it was derived, and which are no longer anything but approximations, if we take perturbations into account. Now why does this principle thus occupy a kind of privileged position among physical laws? There are many reasons for that. At the outset we think that we cannot reject it, or even doubt its absolute rigour, without admitting the possibility of perpetual motion; we certainly feel distrust at such a prospect, and we believe ourselves less rash in affirming it than in denying it. That perhaps is not quite accurate. The impossibility of perpetual motion only implies the conservation of energy for reversible phenomena. The imposing simplicity of Mayer's principle equally contributes to strengthen our faith. In a law immediately de duced from experiments, such as Mariotte's law, this simplicity would rather appear to us a reason for distrust ; but here this is no longer the case. We take elements which at the first glance are unconnected; these arrange themselves in an un expected order, and form a harmonious whole. We cannot believe that this unexpected har mony is a mere result of chance. Our conquest appears to be valuable to us in proportion to the efforts it has cost, and we feel the more certain of having snatched its true secret from Nature in pro portion as Nature has appeared more jealous of our attempts to discover it. But these are only small reasons. Before we raise Mayer's law to the dignity of an absolute principle, a deeper discussion is necessary. But if we embark on this discussion we see that this absolute principle is not even easy to enunciate. In every particular case we clearly see what energy is, and we can give it at least a provisory definition; but it is impossible to find a general definition of it. If we wish to enunciate the principle in all its generality and apply it to the universe, we see it vanish, so to speak, and nothing is left but this — there is something which remains constant. But has this a meaning ? In the determinist hypothesis the state of the uni verse is determined by an extremely large number n of parameters, which I shall call xit x.2, x3 . . . xn. As soon as we know at a given moment the values of these n parameters, we also know their derivatives with respect to time, and we can therefore cal culate the values of these same parameters at an anterior or ulterior moment. In other words, these n parameters specify n differential equations of the first order. These equations have n-i integrals, and therefore there are n-i functions of xi> X2> #3 • . . xMt which remain constant. If we say then, there is something which remains constant, we are only enunciating a tautology. We would be even embarrassed to decide which among all our integrals is that which should retain the name of energy. Besides, it is not in this sense that Mayer's principle is understood when it is applied to a limited system. We admit, then, that p of our n parameters vary independently so that we ENERGY AND THERMODYNAMICS. 133 have only n -p relations, generally linear, between our n parameters and their derivatives. Suppose, for the sake of simplicity, that the sum of the work done by the external forces is zero, as well as that of all the quantities of heat given off from the interior: what will then be the meaning of our principle ? There is a combination of these n -p relations, of which the first member is an exact differential; and then this differential vanishing in virtue of our n—p relations, its integral is a constant, and it is this integral which we call energy. But how can it be that there are several parameters whose variations are independent ? That can only take place in the case of external forces (although \ve have supposed, for the sake of simplicity, that the algebraical sum of all the work done by these forces has vanished). If, in fact, the system were completely isolated from all external action, the values of our n parameters at a given moment would suffice to determine the state of the system at any ulterior moment whatever, provided that we still clung to the determinist hypothesis. We should therefore fall back on the same difficulty as before. If the future state of the system is not entirely determined by its present state, it is because it further depends on the state of bodies external to the system. But then, is it likely that there exist among the parameters % which define the state of the system of equations independent of this state of the external bodies? and if in certain cases we think we can find them, is it not only because of our ignorance, and because the influence of these bodies is too weak for our experiment to be able to detect it ? If the system is not regarded as completely isolated, it is probable that the rigorously exact expression of its internal energy will depend upon the state of the external bodies. Again, I have supposed above that the sum of all the external work is zero, and if we wish to be free from this rather artificial restriction the enunciation becomes still more difficult. To formulate Mayer's principle by giving it an absolute meaning, we must extend it to the whole universe, and then we find ourselves face to face with the very difficulty we have endeavoured to avoid. To sum up, and to use ordinary language, the law of the conservation of energy can have only one significance, because there is in it a property common to all possible properties; but in the determinist hypothesis there is only one possible, and then the law has no meaning. In the indeterminist hypothesis, on the other hand, it would have a meaning even if \ve wished to regard it in an absolute sense. It would appear as a limitation imposed on freedom. But this word warns me that I am wandering from the subject, and that I am leaving the domain of mathematics and physics. I check myself, therefore, and I wish to retain only one impression of the whole of this discussion, and that is, that Mayer's law is a form subtle enough ENERGY AND THERMODYNAMICS. ±35 for us to be able to put into it almost anything we like. I do not mean by that that it corresponds to no objective reality, nor that it is reduced to mere tautology; since, in each particular case, and provided we do not wish to extend it to the absolute, it has a perfectly clear meaning. This subtlety is a reason for believing that it will last long; and as, on the other hand, it will only disappear to be blended in a higher harmony, we may work with confidence and utilise it, certain beforehand that our work will not be lost. Almost everything that I have just said applies to the principle of Clausius. What distinguishes it is, that it is expressed by an inequality. It will be said perhaps that it is the same with all physical laws, since their precision is always limited by errors of observation. But they at least claim to be first approximations, and we hope to replace them little by little by more exact laws. If, on the other hand, the principle of Clausius reduces to an inequality, this is not caused by the imperfection of our means of observation, but by the very nature of the question. General Conclusions on Part III. — The prin ciples of mechanics are therefore presented to us under two different aspects. On the one hand, there are truths founded on experiment, and verified approximately as far as almost isolated systems are concerned ; on the other hand, there are postulates applicable to the whole of the universe and regarded as rigorously true. If these postulates possess a generality and a certainty which falsify the experimental truths from which they were deduced, it is because they reduce in final analysis to a simple con vention that we have a right to make, because we are certain beforehand that no experiment can contradict it. This convention, however, is not absolutely arbitrary; it is not the child of our caprice. \Ye admit it because certain experiments have shown us that it will be con venient, and thus is explained how experiment has built up the principles of mechanics, and why, moreover, it cannot reverse them. Take a comparison with geometry. The fundamental propositions of geometry, for instance, Euclid's postulate, are only conventions, and it is quite as unreasonable to ask if they are true or false as to ask if the metric system is true or false. Only, these conventions are convenient, and there are certain experiments which prove it to us. At the first glance, the analogy is complete, the role of experiment seems the same. We shall there fore be tempted to say, either mechanics must be looked upon as experimental science and then it should be the same with geometry; or, on the contrary, geometry is a deductive science, and then we can say the same of mechanics. Such a conclusion would be illegitimate. The experi ments which have led us to adopt as more ENERGY AND THERMO-DYNAMICS. 137 convenient the fundamental conventions of geometry refer to bodies which have nothing in common with those that are studied by geometry. They refer to the properties of solid bodies and to the propagation of light in a straight line. These are mechanical, optical experiments. In no way can they be regarded as geometrical experiments. And even the probable reason why our geometry seems convenient to us is, that our bodies, our hands, and our limbs enjoy the properties of solid bodies. Our fundamental experiments are pre-eminently physiological experiments which refer, not to the space which is the object that geometry must study, but to our body — that is to say, to the instrument which we use for that study. On the other hand, the fundamental conventions of mechanics and the experiments which prove to us that they are convenient, certainly refer to the same objects or to analogous objects. Conventional and general principles are the natural and direct generalisations of experi mental and particular principles. Let it not be said that I am thus tracing artificial frontiers between the sciences; that I am separating by a barrier geometry properly so called from the study of solid bodies. I might just as well raise a barrier between experimental mechanics and the conventional mechanics of general principles. Who does not see, in fact, that by separating these two sciences we mutilate both, and that what will remain of the conventional mechanics when it is isolated will be but very little, and can in no way be compared with that grand body of doctrine which is called geometry. We now understand why the teaching of mechanics should remain experimental. Thus only can we be made to understand the genesis of the science, and that is indispensable for a complete knowledge of the science itself. Besides, if we study mechanics, it is in order to apply it ; and we can only apply it if it remains objective. Now, as we have seen, when principles gain in generality and certainty they lose in objectivity. It is therefore especially with the objective side of principles that we must be early familiarised, and this can only be by passing from the particular to the general, instead of from the general to the particular. Principles are conventions and definitions in disguise. They are, however, deduced from experimental laws, and these laws have, so to speak, been erected into principles to which our mind attributes an absolute value. Some philosophers have generalised far too much. They have thought that the principles were the whole of science, and therefore that the whole of science was conventional. This para doxical doctrine, which is called Nominalism, cannot stand examination. How can a law become a principle ? It expressed a relation between two real terms, A and B; but it was ENERGY AND THERMODYNAMICS. 139 not rigorously true, it was only approximate. We introduce arbitrarily an intermediate term, C, more or less imaginary, and C is by definition that which has with A exactly the relation expressed by the law. So our law is decomposed into an absolute and rigorous principle which expresses the relation of A to C, and an approximate experi mental and revisable law which expresses the: relation of C to B. But it is clear that however far this decomposition may be carried, laws will always remain. We shall now enter into the domain of laws properly so called. PART IV, NATURE. CHAPTER IX. HYPOTHESES IN PHYSICS. The Role of Experiment and Generalisation. — Experiment is the sole source of truth. It alone can teach us something new ; it alone can give us certainty. These are two points that cannot be questioned. But then, if experiment is every thing, what place is left for mathematical physics ? What can experimental physics do with such an auxiliary — an auxiliary, moreover, which seems useless, and even may be dangerous? However, mathematical physics exists. It has rendered undeniable service, and that is a fact which has to be explained. It is not sufficient merely to observe ; we must use our observations, and for that purpose we must generalise. This is what has always been done, only as the recollec tion of past errors has made man more and more circumspect, he has observed more and more and generalised less and less. Every age has scoffed at its predecessor, accusing it of having generalised HYPOTHESES IN PHYSICS. 141 too boldly and too naively. Descartes used to commiserate the lonians. Descartes in his turn makes us smile, and no doubt some day our children will laugh at us. Is there no way of getting at once to the gist of the matter, and thereby escaping the raillery which we foresee ? Cannot we be content with experiment alone ? No, that is impossible ; that would be a complete misunderstanding of the true character of science. The man of science must work with method. Science is built up of facts, as a house is built of stones ; but an accumulation of facts is no more a science than a heap of stones is a house. Most important of all, the man of science must exhibit foresight. Carlyle has written somewhere some thing after this fashion. " Nothing but facts are of importance. John Lackland passed by here. Here is something that is admirable. Here is a reality for which I would give all the theories in the world."1 Carlyle was a compatriot of Bacon, and, like him, he wished to proclaim his worship of the God of Things as they are. But Bacon would not have said that. That is the language of the historian. The physicist would most likely have said : " John Lackland passed by here. It is all the same to me, for he will not pass this way again." We all know that there are good and bad experiments. The latter accumulate in vain. Whether there are a hundred or a thousand, 1 V. Past and Present, end of Chapter I., Book II.— [TR.] one single piece of work by a real master — by a Pasteur, for example — will be sufficient to sweep them into oblivion. Bacon w7ould have thoroughly understood that, for he invented the phrase experimentuni crucis; but Carlyle would not have under stood it. A fact is a fact. A student has read such and such a number on his thermometer. He has taken no precautions. It does not matter; he has read it, and if it is only the fact which counts, this is a reality that is as much entitled to be called a reality as the peregrinations of King John Lackland. What, then, is a good experiment? It is that which teaches us something more than V an isolated fact. It is that which enables us to predict, and to generalise. Without generalisa tion, prediction is impossible. The circumstances under which one has operated will never again be reproduced simultaneously. The fact observed will never be repeated. All that can be affirmed is that under analogous circumstances an analogous fact will be produced. To predict it, we must therefore invoke the aid of analogy — that is to say, even at this stage, we must generalise. However timid we may be, there must be interpolation. Experiment only gives us a certain number of isolated points. They must be connected by a continuous line, and this is a true generalisation. But more is done. The curve thus traced will pass between and near the points observed; it will not pass through the points themselves. Thus we are not restricted to generalising our HYPOTHESES IN PHYSICS. 143 experiment, we correct it ; and the physicist who would abstain from these corrections, and really content himself with experiment pure and simple, would be compelled to enunciate very extra ordinary laws indeed. Detached facts cannot therefore satisfy us, and that is why our science must be ordered, or, better still, generalised. It is often said that experiments should be made without preconceived ideas. That is impossible. Not only would it make every experiment fruitless, but even if we wished to do so, it could not be done. Every man has his own conception of the world, and this he cannot so easily lay aside. We must, for example, use language, and our language is necessarily steeped in preconceived ideas. Only they are unconscious preconceived ideas, which are a thousand times the most dangerous of all. Shall we say, that if we cause others to intervene of which we are fully conscious, that we shall only aggravate the evil? I do not think so. I am inclined to think that they will serve as ample counterpoises — I was almost going to say antidotes. They will generally disagree, they will enter into conflict one with another, and ipso facto, they will force us to look at things under different aspects. This is enough to free us. He is no longer a slave who can choose his master. Thus, by generalisation, every fact observed enables us to predict a large number of others ; only, we ought not to forget that the first alone is certain, and that all the others are merely probable. However solidly founded a prediction may appear to us, we are never absolutely sure that experiment will not prove it to be baseless if we set to work to verify it. But the probability of its accuracy is often so great that practically we may be content with it. It is far better to predict without certainty, than never to have predicted at all. We should never, therefore, disdain to verify when the opportunity presents itself. But every experiment is long and difficult, and the labourers are few, and the number of facts which we require to predict is enormous ; and besides this mass, the number of direct verifications that we can make will never be more than a negligible quantity. Of this little that we can directly attain we must choose the best. Every experiment must enable us to make a maximum number of predic tions having the highest possible degree of prob ability. The problem is, so to speak, to increase the output of the scientific machine. I may be permitted to compare science to a library which must go on increasing indefinitely; the librarian has limited funds for his purchases, and he must, therefore, strain every nerve not to waste them. Experimental physics has to make the purchases, and experimental physics alone can enrich the library. As for mathematical physics, her duty is to draw up the catalogue. If the catalogue is well done the library is none the richer for it ; but the reader will be enabled to utilise its riches; and also by showing the librarian the gaps in his HYPOTHESES IN PHYSICS. 145 collection, it will help him to make a judicious use of his funds, which is all the more important, inasmuch as those funds are entirely inadequate. That is the role of mathematical physics. It must direct generalisation, so as to increase what I called just now the output of science. By what means it does this, and how it may do it without danger, is what we have now to examine. The Unity oj Nature. — Let us first of all observe that every generalisation supposes in a certain measure a belief in the unity and simplicity of Nature. As far as the unity is concerned, there can be no difficulty. If the different parts of the universe were not as the organs of the same body, they would not re-act one upon the other; they would mutually ignore each other, and we in particular should only know one part. We need not, therefore, ask if Nature is one, but how she is one. As for the second point, that is not so clear. It is not certain that Nature is simple. Can we without danger act as if she were ? There was a time when the simplicity of Mariotte's law was an argument in favour of its accuracy: when Fresnel himself, after having said in a conversation with Laplace that Nature cares naught for analytical difficulties, was compelled to explain his words so as not to give offence to current opinion. Nowadays, ideas have changed considerably ; but those who do not believe that natural laws must be simple, are still often obliged to act as if they did believe it. They cannot entirely dispense with this necessity without making all generalisation, and therefore all science, impossible. It is clear that any fact can be generalised in an infinite number of ways, and it is a question of choice. The choice can only be guided by considerations of simplicity. Let us take the most ordinary case, that of interpola tion. We draw a continuous line as regularly as possible between the points given by observation. Why do we avoid angular points and inflexions that are too sharp ? Why do we not make our curve describe the most capricious zigzags ? It is because we know beforehand, or think we know, that the law we have to express cannot be so complicated as all that. The mass of Jupiter may be deduced either from the movements of his satellites, or from the perturbations of the major planets, or from those of the minor planets. If we take the mean of the determinations obtained by these three methods, we find three numbers very close together, but not quite identical. This result might be interpreted by supposing that the gravitation constant is not the same in the three cases; the observations would be certainly much better represented. Why do we reject this inter pretation ? Not because it is absurd, but because it is uselessly complicated. W7e shall only accept it when we are forced to, and it is not imposed upon us yet. To sum up, in most cases every law is held to be simple until the contrary is proved. HYPOTHESES IN PHYSICS. 147 This custom is imposed upon physicists by the reasons that I have indicated, but how can it be justified in the presence of discoveries which daily show us fresh details, richer and more complex? How can we even reconcile it with the unity of nature ? For if all things are interdependent, the relations in which so many different objects intervene can no longer be simple. If we study the history of science we see pro duced two phenomena which are, so to speak, each the inverse of the other. Sometimes it is simplicity which is hidden under what is apparently complex ; sometimes, on the contrary, it is simplicity which is apparent, and which conceals extremely complex realities. What is there more complicated than the disturbed motions of the planets, and what more simple than Newton's law ? There, as Fresnel said, Nature playing with analytical difficulties, only uses simple means, and creates by their combina tion I know not what tangled skein. Here it is the hidden simplicity which must be disentangled. Examples to the contrary abound. In the kinetic theory of gases, molecules of tremendous velocity are discussed, whose paths, deformed by incessant impacts, have the most capricious shapes, and plough their way through space in every direction. The result observable is Mariotte's simple law. Each individual fact was complicated. The law of great numbers has re-established simplicity in the mean. Here the simplicity is only apparent, and the coarseness of our senses alone prevents us from seeing the complexity. Many phenomena obey a law of proportion ality. But why? Because in these phenomena there is something which is very small. The simple law observed is only the translation of the general analytical rule by which the infinitely small increment of a function is proportional to the increment of the variable. As in reality our increments are not infinitely small, but only very small, the law of proportionality is only approximate, and simplicity is only apparent. What I have just said applies to the law of the superposition of small movements, which is so fruitful in its applications and which is the founda tion of optics. And Newton's law itself? Its simplicity, so long undetected, is perhaps only apparent. Who knows if it be not due to some complicated mechanism, to the impact of some subtle matter animated by irregular movements, and if it has not become simple merely through the play of averages and large numbers? In any case, it is difficult not to suppose that the true law con tains complementary terms which may become sensible at small distances. If in astronomy they are negligible, and if the law thus regains its simplicity, it is solely on account of the enormous distances of the celestial bodies. No doubt, if our means of investigation became more and more penetrating, we should discover the simple beneath HYPOTHESES IN PHYSICS. 149 the complex, and then the complex from the simple, and then again the simple beneath the complex, and so on, without ever being able to predict what the last term will be. We must stop somewhere, and for science to be possible we must stop where we have found simplicity. That is the only ground on which we can erect the edifice of our generalisations. But, this simplicity being only apparent, will the ground be solid enough ? That is what we have now to discover. For this purpose let us see what part is played in our generalisations by the belief in simplicity. We have verified a simple law in a considerable number of particular cases. We refuse to admit that this coincidence, so often repeated, is a result of mere chance, and we conclude that the law must be true in the general case. Kepler remarks that the positions of a planet observed by Tycho are all on the same ellipse. Not for one moment does he think that, by a singular freak of chance, Tycho had never looked at the heavens except at the very moment when the path of the planet happened to cut that ellipse. What does it matter then if the simplicity be real or if it hide a complex truth ? Whether it be due to the influence of great numbers which reduces individual differences to a level, or to the greatness or the smallness of certain quantities which allow of certain terms to be neglected — in no case is it due to chance. This simplicity, real or apparent, has always a cause. We shall therefore always be able to reason in the same fashion, and if a simple law has been observed in several particular cases, we may legitimately suppose that it still will be true in analogous cases. To refuse to admit this would be to attribute an in admissible role to chance. However, there is a difference. If the simplicity were real and pro found it would bear the test of the increasing precision of our methods of measurement. If, then, we believe Nature to be profoundly simple, we must conclude that it is an approximate and not a rigorous simplicity. This is what was formerly done, but it is what we have no longer the right to do. The simplicity of Kepler's laws, for instance, is only apparent ; but that does not prevent them from being applied to almost all systems analogous to the solar system, though that prevents them from being rigorously exact. Role of Hypothesis. — Every generalisation is a hypothesis. Hypothesis therefore plays a neces sary role, which no one has ever contested. Only, it should always be as soon as possible submitted to verification. It goes without saying that, if it cannot stand this test, it must be abandoned without any hesitation. This is, indeed, what is generally done; but sometimes with a certain impatience. Ah well ! this impatience is not justified. The physicist who has just given up one of his hypotheses should, on the contrary, rejoice, for he found an unexpected opportunity of discovery. His hypothesis, I imagine, had not HYPOTHESES IN PHYSICS. 151 been lightly adopted, It took into account all the known factors which seem capable of intervention in the phenomenon. If it is not verified, it is because there is something unexpected and extra ordinary about it, because we are on the point of finding something unknown and new. Has the hypothesis thus rejected been sterile ? Far from it. It may be even said that it has rendered more service than a true hypothesis. Not only has it been the occasion of a decisive experiment, but if this experiment had been made by chance, without the hypothesis, no conclusion could have been drawn ; nothing extraordinary would have been seen ; and only one fact the more would have been catalogued, without deducing from it the remotest consequence. Now, under what conditions is the use of hypothesis without danger ? The proposal to submit all to experiment is not sufficient. Some hypotheses are dangerous, — first and foremost those which are tacit and unconscious. And since we make them without knowing them, we cannot get rid of them. Here again, there is a service that mathematical physics may render us. By the precision which is its char acteristic, we are compelled to formulate all the hypotheses that we would unhesitatingly make without its aid. Let us also notice that it is important not to multiply hypotheses indefinitely. If we construct a theory based upon multiple hypo theses, and if experiment condemns it, which of the premisses must be changed ? It is impossible to tell. Conversely, if the experiment succeeds, must we suppose that it has verified all these hypotheses at once ? Can several unknowns be determined from a single equation ? I We must also take care to distinguish between ' the different kinds of hypotheses. First of all, there are those wrhich are quite natural and ( necessary. It is difficult not to suppose that the influence of very distant bodies is quite negligible, that small movements obey a linear law, and that effect is a continuous function of its cause. I will say as much for the conditions imposed by symmetry. All these hypotheses affirm, so to speak, the common basis of all the theories of mathematical physics. They are the last that should be abandoned. There is a second category of hypotheses which I shall qualify as indifferent. In most questions the analyst assumes, at the beginning of his calculations, either that matter is continuous, or the reverse, that it is formed of atoms. In either case, his results would have been the same. On the atomic supposition he has a little more difficulty in obtaining them — that is all. If, then, experiment confirms his conclusions, will he suppose that he has proved, for example, the real existence of atoms ? In optical theories two vectors are introduced, one of which we consider as a velocity and the other as a vortex. This again is an indifferent hypothesis, since we should have arrived at the HYPOTHESES TN PHYSICS. 153 same conclusions by assuming the former to be a vortex and the latter to be a velocity. The success of the experiment cannot prove, therefore, that the first vector is really a velocity. It only proves one thing — namely, that it is a vector; and that is the only hypothesis that has really been introduced into the premisses. To give it the concrete appearance that the fallibility of our minds demands, it was necessary to consider it either as a velocity or as a vortex. In the same way, it was necessary to represent it by an x or a y, but. the result will not prove that we were right or wrong in regarding it as a velocity; nor will it prove we are right or wrong in calling it x and not y. These indifferent hypotheses are never danger ous provided their characters are not misunder stood. They may be useful, either as artifices for calculation, or to assist our understanding by concrete images, to fix the ideas, as we say. They need not therefore be rejected. The hypotheses of the third category are real generalisations. They must be confirmed or invalidated by experi ment. Whether verified or condemned, they will always be fruitful; but, for the reasons I have given, they will only be so if they are not too numerous. Origin of Mathematical Physics. — Let us go further and study more closely the conditions which have assisted the development of mathe matical physics. We recognise at the outset that the efforts of men of science have always tended to resolve the complex phenomenon given directly by experiment into a very large number of ele mentary phenomena, and that in three different ways. First, with respect to time. Instead of embracing in its entirety the progressive development of a phenomenon, we simply try to connect each moment with the one immediately preceding. We admit that the present state of the world only depends on the immediate past, without being directly influenced, so to speak, by the recollection of a more distant past. Thanks to this postulate, instead of studying directly the whole succession of phenomena, we may confine ourselves to writing down its differential equation; for the laws of Kepler we substitute the law of Newton. Next, we try to decompose the phenomena in space. What experiment gives us is a confused aggregate of facts spread over a scene of consider able extent. We must try to deduce the element ary phenomenon, which will still be localised in a very small region of space. A few examples perhaps will make my meaning clearer. If \ve wished to study in all its com plexity the distribution of temperature in a cooling solid, we could never do so. This is simply be cause, if we only reflect that a point in the solid can directly impart some of its heat to a neigh bouring point, it will immediately impart that HYPOTHESES IN PHYSICS. 155 heat only to the nearest points, and it is but gradually that the flow of heat will reach other portions of the solid. The elementary pheno menon is the interchange of heat between two contiguous points. It is strictly localised and relatively simple if, as is natural, we admit that it is not influenced by the temperature of the molecules whose distance apart is small. I bend a rod: it takes a very complicated form, the direct investigation of which would be im possible. But I can attack the problem, however, if I notice that its flexure is only the resultant of the deformations of the very small elements of the rod, and that the deformation of each of these elements only depends on the forces which are directly applied to it, and not in the least on those which may be acting on the other elements. In all these examples, which may be increased without difficulty, it is admitted that there is no action at a distance or at great distances. That is an hypothesis. It is not always true, as the law of gravitation proves. It must therefore be verified. If it is confirmed, even approximately, it is valu able, for it helps us to use mathematical physics, at any rate by successive approximations. If it does not stand the test, we must seek something else that is analogous, for there are other means of arriving at the elementary phenomenon. If several bodies act simultaneously, it may happen that their actions are independent, and may be added one to the other, either as vectors or as scalar quantities. The elementary phenomenon is then the action of an isolated body. Or suppose, again, it is a question of small movements, or more generally of small variations which obey the wellknown law of mutual or relative independence. The movement observed will then be decomposed into simple movements — for example, sound into its harmonics, and white light into its monochro matic components. When we have discovered in which direction to seek for the elementary pheno mena, by what means may we reach it ? First, it will often happen that in order to predict it, or rather in order to predict what is useful to us, it will not be necessary to know its mechanism. The law of great numbers will suffice. Take for example the propagation of heat. Each molecule radiates to wards its neighbour — we need not inquire accord ing to what law; and if we make any supposition in this respect, it will be an indifferent hypothesis, and therefore useless and unverifiable. In fact, by the action of averages and thanks to the symmetry of the medium, all differences are levelled, and, whatever the hypothesis may be, the result is always the same. The same feature is presented in the theory of elasticity, and in that of capillarity. The neigh bouring molecules attract and repel each other, we need not inquire by what law. It is enough for us that this attraction is sensible at small distances only, and that the molecules are very numerous, that the medium is symmetrical, and we have HYPOTHESES IN PHYSICS. 157 only to let the law of great numbers come into play. Here again the simplicity of the elementary phenomenon is hidden beneath the complexity of the observable resultant phenomenon; but in its turn this simplicity was only apparent and dis guised a very complex mechanism. Evidently the best means of reaching the elementary pheno menon would be experiment. It would be neces sary by experimental artifices to dissociate the complex system which nature offers for our in vestigations and carefully to study the elements as dissociated as possible; for example, natural white light would be decomposed into monochromatic lights by the aid of the prism, and into polarised lights by the aid of the polariser. Unfortunately, that is neither always possible nor always suffi cient, and sometimes the mind must run ahead of experiment. I shall only give one example which has always struck me rather forcibly. If I de compose white light, I shall be able to isolate a portion of the spectrum, but however small it may be, it will always be a certain width. In the same way the natural lights which are called mono chromatic give us a very fine array, but a y which is not, however, infinitely fine. It might be supposed that in the experimental study of the properties of these natural lights, by operating with finer and finer rays, and passing on at last to the limit, so to speak, we should eventually obtain the properties of a rigorously monochromatic light. That would not be accurate. I assume that two rays emanate from the same source, that they are first polarised in planes at right angles, that they are then brought back again to the same plane of polarisation, and that we try to obtain interference. If the light were rigorously monochromatic, there would be inter ference; but with our nearly monochromatic lights, there will be no interference, and that, however narrow the ray may be. For it to be otherwise, the ray would have to be several million times finer than the finest known rays. Here then we should be led astray by proceeding to the limit. The mind has to run ahead of the experiment, and if it has done so with success, it is because it has allowed itself to be guided by the instinct of simplicity. The knowledge of the ele mentary fact enables us to state the problem in the form of an equation. It only remains to de duce from it by combination the observable and verifiable complex fact. That is what we call integration, and it is the province of the mathe matician. It might be asked, why in physical science generalisation so readily takes the mathematical form. The reason is now easy to see. It is not only because we have to express numerical laws; it is because the observable phenomenon is due to the superposition of a large number of elementary phenomena which are all similar to each other ; and in this way differential equations are quite naturally introduced. It is HYPOTHESES IN PHYSICS. I5Q not enough that each elementary phenomenon should obey simple laws: all those that we have to combine must obey the same law; then only is the intervention of mathematics of any use. Mathematics teaches us, in fact, to combine like with like. Its object is to divine the result of a combination without having to reconstruct that combination element by element. If we have to repeat the same operation several times, mathe matics enables us to avoid this repetition by telling the result beforehand by a kind of induction. This I have explained before in the chapter on mathematical reasoning. But for that purpose all these operations must be similar; in the con trary case we must evidently make up our minds to working them out in full one after the other, and mathematics will be useless. It is therefore, thanks to the approximate homogeneity of the matter studied by physicists, that mathematical physics came into existence. In the natural sciences the following conditions are no longer to be found: — homogeneity, relative independence of remote parts, simplicity of the elementary fact; and that is why the student of natural science is compelled to have recourse to other modes of generalisation. CHAPTER X. THE THEORIES OF MODERN PHYSICS, Significance of Physical Theories. — The ephemeral nature of scientific theories takes by surprise the man of the world. Their brief period of prosperity ended, he sees them abandoned one after another ; he sees ruins piled upon ruins; he predicts that the theories in fashion to-day will in a short time succumb in their turn, and he concludes that they are absolutely in vain. This is what he calls the bankruptcy of science. His scepticism is superficial ; he does not take into account the object of scientific theories and the part they play, or he would understand that the ruins may be still good for something. No theory seemed established on firmer ground than Fresnel's, which attributed light to the move ments of the ether. Then if Maxwell's theory is to-day preferred, does that mean that Fresnel's work was in vain ? No; for Fresnel's object was not to know whether there really is an ether, if it is or is not formed of atoms, if these atoms really move in this way or that; his object was to predict optical phenomena. This Fresnel's theory enables us to do to- THE THEORIES OF MODERN PHYSICS. l6l day as well as it did before Maxwell's time. The differential equations are always true, they may be always integrated by the same methods, and the results of this integration still preserve their value. It cannot be said that this is reducing physical theories to simple practical recipes ; these equations express relations, and if the equations remain true, it is because the relations preserve their reality. They teach us now, as they did then, that there is such and such a relation between this thing and that ; only, the something which we then called motion, we now call electric current. But these are merely names of the images we substituted for the real objects which Nature will hide for ever from our eyes. The true relations between these real objects are the only reality we can attain, and the sole condition is that the same relations shall exist between these objects as between the images we are forced to put in their place. If the relations are known to us, what does it matter if we think it convenient to replace one image by another ? That a given periodic phenomenon (an electric oscillation, for instance) is really due to the vibration of a given atom, which, behaving like a pendulum, is really displaced in this manner or that, all this is neither certain nor essential. But that there is between the electric oscillation, the movement of the pendulum, and all periodic phenomena an intimate relationship which corre sponds to a profound reality; that this relationship, this similarity, or rather this parallelism, is con tinued in the details ; that it is a consequence of more general principles such as that of the con servation of energy, and that of least action ; this we may affirm ; this is the truth which will ever remain the same in whatever garb we may see fit to clothe it. Many theories of dispersion have been proposed. The first were imperfect, and contained but little truth. Then came that of Helmholtz, and this in its turn was modified in different ways ; its author himself conceived another theory, founded on Maxwell's principles. But the remarkable thing is, that all the scientists who followed Helmholtz obtain the same equations, although their starting-points were to all appearance widely separated. I venture to say that these theories are all simultaneously truje; not merely because they express a true relation — that between absorp tion and abnormal dispersion. In the premisses of these theories the part that is true is the part common to all: it is the affirmation of this or that relation between certain things, which some call by one name and some by another. The kinetic theory of gases has given rise to many objections, to which it would be difficult to find an answer were it claimed that the theory is absolutely true. But all these objections do not alter the fact that it has been useful, particularly in revealing to us one true relation which would otherwise have remained profoundly THE THEORIES OF MODERN PHYSICS. 163 hidden — the relation between gaseous and osmotic pressures. In this sense, then, it may be said to be true. When a physicist finds a contradiction between two theories which are equally dear to him, he sometimes says: " Let us not be troubled, but let us hold fast to the two ends of the chain, lest we lose the intermediate links." This argument of the embarrassed theologian would be ridiculous if we were to attribute to physical theories the interpretation given them by the man of the world. In case of contradiction one of them at least should be considered false. But this is no longer the case if we only seek in them what should be sought. It is quite possible that they both express true relations, and that the contra dictions only exist in the images we have formed to ourselves of reality. To those who feel that we are going too far in our limitations of the domain accessible to the scientist, I reply: These questions which we forbid you to investigate, and which you so regret, are not only insoluble, they are illusory and devoid of meaning. Such a philosopher claims that all physics can be explained by the mutual impact of atoms. If he simply means that the same relations obtain between physical phenomena as between ~the mutual impact of a large number of billiard balls — well and good! this is verifiable, and perhaps is true. But he means something more, and we think we understand him, because we think we know what an impact is. Why? Simply because we have often watched a game of billiards. Are we to understand that God experiences the same sensations in the contemplation of His work that we do in watching a game of billiards ? If it is not our intention to give his assertion this fantastic meaning, and if we do not wish to give it the more restricted meaning I have already mentioned, which is the sound meaning, then it has no meaning at all. Hypotheses of this kind have therefore only a metaphorical sense. The scientist should no more banish them than a poet banishes metaphor; but he ought to know what they are worth. They may be useful to give satisfaction to the mind, and they will do no harm as long as they are only indifferent hypotheses. These considerations explain to us why certain theories, that were thought to be abandoned and definitively condemned by experiment, are suddenly revived from their ashes and begin a new life. It is because they expressed true relations, and had not ceased to do so when for some reason or other we felt it necessary to enunciate the same relations in another language. Their life had been latent, as it were. Barely fifteen years ago, was there anything more ridiculous, more quaintly old-fashioned, than the fluids of Coulomb ? And yet, here they are re-appearing under the name of electrons. In what do these permanently electrified molecules differ THE THEORIES OF MODERN PHYSICS. 165 from the electric molecules of Coulomb ? It is true that in the electrons the electricity is sup ported by a little, a very little matter ; in other words, they have mass. Yet Coulomb did not deny mass to his fluids, or if he did, it was with reluctance. It would be rash to affirm that the belief in electrons will not also undergo an eclipse, but it was none the less curious to note this un expected renaissance. But the most striking example is Carnot's principle. Carnot established it, starting from false hypotheses. When it was found that heat was indestructible, and may be converted into work, his ideas were completely abandoned ; later, Clausius returned to them, and to him is due their definitive triumph. In its primitive form, Carnot's theory expressed in addition to true relations, other inexact relations, the debris of old ideas ; but the presence of the latter did not alter the reality of the others. Clausius had only to separate them, just as one lops off dead branches. The result was the second fundamental law of thermodynamics. The relations were always the same, although they did not hold, at least to all appearance, between the same objects. This was sufficient for the principle to retain its value. Nor have the reasonings of Carnot perished on this account ; they were applied to an imperfect conception of matter, but their form — i.e., the essential part of them, remained correct. What I have just said throws some light at the same time on the role of general principles, such as those of the principle of least action or of the conservation of energy. These principles are of very great value. They were obtained in the search for what there was in common in the enunciation of numerous physical laws ; they thus represent the quintessence of innumerable observations. However, from their very generality results a consequence to which I have called attention in Chapter VIII. — namely, that they are no longer capable of verification. As we cannot give a general definition of energy, the principle of the conservation of energy simply signifies that there is a something which remains constant. Whatever fresh notions of the world may be given us by future experiments, we are certain beforehand that there is something which remains constant, and which may be called energy. Does this mean that the principle has no meaning and vanishes into a tautology ? Not at all. It means that the different things to which we give the name of energy are connected by a true relation ship ; it affirms between them a real relation. But then, if this principle has a meaning, it may be false ; it may be that we have no right to extend indefinitely its applications, and yet it is certain beforehand to be verified in the strict sense of the word. How, then, shall we know when it has been extended as far as is legitimate ? Simply when it ceases to be useful to us — i.e., THE THEORIES OF MODERN PHYSICS. 167 when we can no longer use it to predict correctly new phenomena. We shall be certain in such a case that the relation affirmed is no longer real, for otherwise it would be fruitful ; experiment without directly contradicting a new extension of the principle will nevertheless have condemned it. Physics and Mechanism. — Most theorists have a constant predilection for explanations borrowed from physics, mechanics, or dynamics. Some \vould be satisfied if they could account for all phenomena by the motion of molecules attracting one another according to certain laws. Others are more exact : they would suppress attractions acting at a distance ; their molecules would follow rectilinear paths, from which they would only be deviated by impacts. Others again, such as Hertz, suppress the forces as well, but suppose their molecules subjected to geometrical connections analogous, for instance, to those of articulated systems; thus, they wish to reduce dynamics to a kind of kinematics. In a word, they all wish to bend nature into a certain form, and unless they can do this they cannot be satisfied. Is Nature flexible enough for this ? We shall examine this question in Chapter XII., apropos of Maxwell's theory. Every time that the principles of least action and energy are satisfied, we shall see that not only is there always a mechanical explanation possible, but that there is an unlimited number of such explanations. By means of a well-known theorem due to Konigs, it may be shown that we can explain everything in an unlimited number of ways, by connections after the manner of Hertz, or, again, by central forces. No doubt it may be just as easily de monstrated that everything may be explained by simple impacts. For this, let us bear in mind that it is not enough to be content with the ordinary matter of which we are aware by means of our senses, and the movements of which we observe directly. We may conceive of ordinary matter as either composed of atoms, whose internal movements escape us, our senses being able to estimate only the displacement of the whole ; or we may imagine one of those subtle fluids, which under the name of ether or other names, have from all time played so important a role in physical theories. Often we go further, and regard the ether as the only primitive, or even as the only true matter. The more moderate consider ordinary matter to be condensed ether, and there is nothing startling in this conception; but others only reduce its importance still further, and see in matter nothing more than the geo metrical locus of singularities in the ether. Lord Kelvin, for instance, holds what we call matter to be only the locus of those points at which the ether is animated by vortex motions. Riemann believes it to be locus of those points at which ether is constantly destroyed ; to Wiechert or Larmor, it is the locus of the points at which the ether has undergone a kind of torsion of a THE THEORIES OF MODERN PHYSICS. l6g very particular kind. Taking any one of these points of view, I ask by what right do we apply to the ether the mechanical properties observed in ordinary matter, which is but false matter ? The ancient fluids, caloric, electricity, etc., were abandoned when it was seen that heat is not indestructible. But they were also laid aside for another reason, In materialising them, their individuality was, so to speak, emphasised — gaps were opened between them ; and these gaps had to be filled in when the sentiment of the unity of Nature became stronger, and when the intimate relations which connect all the parts were per ceived. In multiplying the fluids, not only did the ancient physicists create unnecessary entities, but they destroyed real ties. It is not enough for a theory not to affirm false relations ; it must not conceal true relations. Does our ether actually exist ? We know the origin of our belief in the ether. If light takes several years to reach us from a distant star, it is no longer on the star, nor is it on the earth. It must be somewhere, and supported, so to speak, by some material agency. The same idea may be expressed in a more mathematical and more abstract form. What we note are the changes undergone by the material molecules. We see, for instance, that the photo graphic plate experiences the consequences of a phenomenon of which the incandescent mass of a star was the scene several vears before. Now, in ordinary mechanics, the state of the system under consideration depends only on its state at the moment immediately preceding; the system therefore satisfies certain differential equations. On the other hand, if we did not believe in the ether, the state of the material universe would depend not only on the state immediately pre ceding, but also on much older states ; the system would satisfy equations of finite differences. The ether was invented to escape this breaking down of the laws of general mechanics. Still, this would only compel us to fill the interplanetary space with ether, but not to make it penetrate into the midst of the material media. Fizeau's experiment goes further. By the interference of rays which have passed through the air or water in motion, it seems to show us two different media penetrating each other, and yet being displaced with respect to each other. The ether is all but in our grasp. Experiments can be conceived in which we come closer still to it. Assume that Newton's principle of the equality of action and re-action is not true if applied to matter alone, and that this can be proved. The geometrical sum of all the forces applied to all the molecules would no longer be zero. If we did not wish to change the whole of the science of mechanics, we should have to introduce the ether, in order that the action which matter apparently undergoes should be counterbalanced by the re-action of matter on something. THE THEORIES OF MODERN PHYSICS. IJI Or again, suppose we discover that optical and electrical phenomena are influenced by the motion of the earth. It would follow that those pheno mena might reveal to us not only the relative motion of material bodies, but also what would seem to be their absolute motion. Again, it would be necessary to have an ether in order that these so-called absolute movements should not be their displacements with respect to empty space, but with respect to something concrete. Will this ever be accomplished ? I do not think so, and I shall explain why; and yet, it is not absurd, for others have entertained this view. For instance, if the theory of Lorentz, of which I shall speak in more detail in Chapter XIII., were true, Newton's principle would not apply to matter alone, and the difference would not be very far from being within reach of experiment. On the other hand, many experiments have been made on the influence of the motion of the earth. The results have always been negative. But if these experiments have been undertaken, it is because we have not been certain beforehand; and indeed, according to current theories, the compensation would be only approximate, and we might expect to find accurate methods giving positive results. I think that such a hope is illusory ; it was none the less interesting to show that a success of this kind would, in a certain sense, open to us a new world. And now allow me to make a digression ; I must explain why I do not believe, in spite of Lorentz, that more exact observations will ever make evident anything else but the relative dis placements of material bodies. Experiments have been made that should have disclosed the terms of the first order; the results were nugatory. Could that have been by chance ? No one has admitted this ; a general explanation was sought, and Lorentz found it. He showed that the terms of the first order should cancel each other, but not the terms of the second order. Then more exact experiments were made, which were also negative ; neither could this be the result of chance. An explanation was necessary, and was forthcoming ; they always are ; hypotheses are what we lack the least. But this is not enough. Who is there who does not think that this leaves to chance far too important a role ? Would it not also be a chance that this singular concurrence should cause a certain circumstance to destroy the terms of the first order, and that a totally different but very opportune circumstance should cause those of the second order to vanish? No; the same explanation must be found for the two cases, and everything tends to show that this explanation would serve equally well for the terms of the higher order, and that the mutual destruction of these terms will be rigorous and absolute. The Present State of Physics. — Two opposite tendencies may be distinguished in the history THE THEORIES OF MODERN PHYSICS. 173 of the development of physics. On the one hand, new relations are continually being discovered between objects which seemed destined to remain for ever unconnected ; scattered facts cease to be strangers to each other and tend to be marshalled into an imposing synthesis. The march of science is towards unity and simplicity. On the other hand, new phenomena are con tinually being revealed ; it will be long before they can be assigned their place — sometimes it may happen that to find them a place a corner of the edifice must be demolished. In the same way, we are continually perceiving details ever more varied in the phenomena we know, where our crude senses used to be unable to detect any lack of unity. What we thought to be simple becomes complex, and the march of science seems to be towards diversity and complication. Here, then, are two opposing tendencies, each of which seems to triumph in turn. Which will win ? If the first wins, science is possible ; but nothing proves this a priori, and it may be that after unsuccessful efforts to bend Nature to our ideal of unity in spite of herself, we shall be submerged by the ever-rising flood of our new riches and com pelled to renounce all idea of classification — to abandon our ideal, and to reduce science to the mere recording of innumerable recipes. In fact, we can give this question no answer. All that we can do is to observe the science of to-day, and compare it with that of yesterday. No doubt after this examination we shall be in a position to offer a few conjectures. Half-a-century ago hopes ran high indeed. The unity of force had just been revealed to us by the discovery of the conservation of energy and of its transformation. This discovery also showed that the phenomena of heat could be explained by molecular movements. Although the nature of these movements was not exactly known, no one doubted but that they would be ascertained before long. As for light, the work seemed entirely com pleted. So far as electricity was concerned, there was not so great an advance. Electricity had just annexed magnetism. This was a considerable and a definitive step towards unity. But how was electricity in its turn to be brought into the general unity, and how was it to be included in the general universal mechanism ? No one had the slightest idea. As to the possibility of the in clusion, all were agreed ; they had faith. Finally, as far as the molecular properties of material bodies are concerned, the inclusion seemed easier, but the details were very hazy. In a word, hopes were vast and strong, but vague. To-day, what do we see ? In the first place, a step in advance — immense progress. The relations between light and electricity are now known ; the three domains of light, electricity, and magnetism, formerly separated, are now one ; and this annexa tion seems definitive. Nevertheless the conquest has caused us some THE THEORIES OF MODERN PHYSICS. 175 sacrifices. Optical phenomena become particular cases in electric phenomena; as long as the former remained isolated, it was easy to explain them by movements which were thought to be known in all their details. That was easy enough ; but any explanation to be accepted must now cover the whole domain of electricity. This cannot be done without difficulty. The most satisfactory theory is that of Lorentz; it is unquestionably the theory that best explains the known facts, the one that throws into relief the greatest number of known relations, the one in which we find most traces of definitive construc tion. That it still possesses a serious fault I have shown above. It is in contradiction with Newton's law that action and re-action are equal and opposite — or rather, this principle according to Lorentz cannot be applicable to matter alone ; if it be true, it must take into account the action of the ether on matter, and the re-action of the matter on the ether. Now, in the new order, it is very likely that things do not happen in this way. However this may be, it is due to Lorentz that the results of Fizeau on the optics of moving bodies, the laws of normal and abnormal dis persion and of absorption are connected with each other and with the other properties of the ether, by bonds which no doubt will not be readily severed. Look at the ease with which the new Zeeman phenomenon found its place, and even aided the classification of Faraday's magnetic rotation, which had defied all Maxwell's efforts. This facility proves that Lorentz's theory is not a mere artificial combination which must eventually find its solvent. It will probably have to be modified, but not destroyed. The only object of Lorentz was to include in a single whole all the optics and electro-dynamics of moving bodies ; he did not claim to give a mechanical explanation. Larmor goes further ; keeping the essential part of Lorentz's theory, he grafts upon it, so to speak, MacCullagh's ideas on the direction of the movement of the ether. MacCullagh held that the velocity of the ether is the same in magnitude and direction as the magnetic force. Ingenious as is this attempt, the fault in Lorentz's theory remains, and is even aggravated. According to Lorentz, we do not know what the movements of the ether are; and because we do not know this, we may suppose them to be movements compensating those of matter, and re-affirming that action and re-action are equal and opposite. According to Larmor we know the movements of the ether, and we can prove that the compensation does not take place. If Larmor has failed, as in my opinion he has, does it necessarily follow that a mechanical ex planation is impossible ? Far from it. I said above that as long as a phenomenon obeys the two principles of energy and least action, so long it allows of an unlimited number of mechanical THE THEORIES OF MODERN PHYSICS. 177 explanations. And so with the phenomena of optics and electricity. But this is not enough. For a mechanical explanation to be good it must be simple ; to choose it from among all the explanations that are possible there must be other reasons than the necessity of making a choice. Well, we have no theory as yet which will satisfy this condition and consequently be of any use. Are we then to complain ? That would be to forget the end we seek, which is not the mechanism ; the true and only aim is unity. We ought therefore to set some limits to our ambition. Let us not seek to formulate a mechanical explanation ; let us be content to show that we can always find one if we wish. In this we have succeeded. The principle of the conservation of energy has always been confirmed, and now it has a fellow in the principle of least action, stated in the form appropriate to physics. This has also been verified, at least as far as concerns the reversible phenomena which obey Lagrange's equations — in other words, which obey the most general laws of physics. The irreversible phenomena are much more difficult to bring into line ; but they, too, are being co-ordinated and tend to come into the unity. The light which illuminates them comes from Carnot's principle. For a long time thermo-dynamics was confined to the study of the dilatations of bodies and of their change of state. For some time past it has been growing bolder, and has considerably extended its domain. We owe to it the theories of the voltaic cell and of their thermo-electric phenomena; there is not a corner in physics which it has not ex plored, and it has even attacked chemistry itself. The same laws hold good ; everywhere, disguised in some form or other, we find Carnot's principle ; everywhere also appears that eminently abstract concept of entropy which is as universal as the concept of energy, and like it, seems to conceal a reality. It seemed that radiant heat must escape, but recently that, too, has been brought under the same laws. In this way fresh analogies are revealed which may be often pursued in detail ; electric resistance resembles the viscosity of fluids ; hysteresis would rather be like the friction of solids. In all cases friction appears to be the type most imitated by the most diverse irreversible phenomena, and this relationship is real and profound. A strictly mechanical explanation of these phenomena has also been sought, but, owing to their nature, it is hardly likely that it will be found. To find it, it has been necessary to suppose that the irreversibility is but apparent, that the elementary phenomena are reversible and obey the known laws of dynamics. But the elements are extremely numerous, and become blended more and more, so that to our crude sight all appears to tend towards uniformity — i.e., all seems to progress in the same direction, and that without THE THEORIES OF MODERN PHYSICS. 179 hope of return. The apparent irreversibility is therefore but an effect of the law of great numbers. Only a being of infinitely subtle senses, such as Maxwell's demon, could unravel this tangled skein and turn back the course of the universe. This conception, which is connected with the kinetic theory of gases, has cost great effort and has not, on the whole, been fruitful ; it may become so. This is not the place to examine if it leads to contradictions, and if it is in conformity with the true nature of things. Let us notice, however, the original ideas of M. Gouy on the Brownian movement. According to this scientist, this singular movement does not obey Carnot's principle. The particles which it sets moving would be smaller than the meshes of that tightly drawn net; they would thus be ready to separate them, and thereby to set back the course of the universe. One can almost see Maxwell's demon at work.1 To resume, phenomena long known are gradually being better classified, but new phenomena come to claim their place, and most of them, like the Zeeman effect, find it at once. Then we have the cathode rays, the X-rays, uranium and radium rays; in fact, a whole world of which none had suspected the existence. How many unexpected 1 Clerk-Maxwell imagined some supernatural agency at work, sorting molecules in a gas of uniform temperature into (a] those possessing kinetic energy above the average, (/;) those possessing kinetic energy below the average. — [Tk.] guests to find a place for ! No one can yet predict the place they will occupy, but I do not believe they will destroy the general unity : I think that they will rather complete it. On the one hand, indeed, the new radiations seem to be connected with the phenomena of luminosity; not only do they excite fluorescence, but they sometimes come into existence under the same conditions as that property; neither are they unrelated to the cause which produces the electric spark under the action of ultra-violet light. Finally, and most important of all, it is believed that in all these phenomena there exist ions, animated, it is true, with velocities far greater than those of electrolytes. All this is very vague, but it will all become clearer. Phosphorescence and the action of light on the spark were regions rather isolated, and consequently somewhat neglected by investigators. It is to be hoped that a new path will now be made which will facilitate their communications with the rest of science. Not only do we discover new phenomena, but those we think we know are revealed in unlooked-for aspects. In the free ether the laws preserve their majestic simplicity, but matter properly so called seems more and more complex ; all we can say of it is but approximate, and our formulae are constantly requiring new terms. But the ranks are unbroken, the relations that we have discovered between objects we thought simple still hold good between the same objects THE THEORIES OF MODERN PHYSICS. l8l when their complexity is recognised, and that alone is the important thing. Our equations become, it is true, more and more complicated, so as to embrace more closely the complexity of nature ; but nothing is changed in the relations which enable these equations to be derived from each other. In a word, the form of these equations persists. Take for instance the laws of reflection. Fresnel established them by a simple and attractive theory which experiment seemed to confirm. Sub sequently, more accurate researches have shown that this verification was but approximate; traces of elliptic polarisation were detected everywhere. But it is owing to the first approximation that the cause of these anomalies was found in the existence of a transition layer, and all the essentials of Fresnel's theory have remained. We cannot help reflecting that all these relations would never have been noted if there had been doubt in the first place as to the complexity of the objects they connect. Long ago it was said: If Tycho had had instruments ten times as precise, we would never have had a Kepler, or a Newton, or Astronomy. It is a misfortune for a science to be born too late, when the means of observation have become too perfect. That is what is happening at this moment with respect to physical chemistry; the founders are hampered in their general grasp by third and fourth decimal places; happily they are men of robust faith. As we get to know the properties of matter better we see that continuity reigns. From the work of Andrews and Van der Waals, we see how the transition from the liquid to the gaseous state is made, and that it is not abrupt. Similarly, there is no gap between the liquid and solid states, and in the proceedings of a recent Congress we see memoirs on the rigidity of liquids side by side with papers on the flow of solids. With this tendency there is no doubt a loss of simplicity. Such and such an effect was represented by straight lines; it is nowr necessary to connect these lines by more or less complicated curves. On the other hand, unity is gained. Separate categories quieted but did not satisfy the mind. Finally, a new domain, that of chemistry, has been invaded by the method of physics, and we see the birth of physical chemistry. It is still quite young, but already it has enabled us to connect such phenomena as electrolysis, osmosis, and the movements of ions. From this cursory exposition what can we con clude? Taking all things into account, we have approached the realisation of unity. This has not been done as quickly as was hoped fifty years ago, and the path predicted has not always been followed; but, on the whole, much ground has been gained. CHAPTER XL THE CALCULUS OF PROBABILITIES. No doubt the reader will be astonished to find reflections on the calculus of probabilities in such a volume as this. What has that calculus to do with physical science ? The questions I shall raise —without, however, giving them a solution — are naturally raised by the philosopher who is examin ing the problems of physics. So far is this the case, that in the two preceding chapters I have several times used the words "probability" and "chance." " Predicted facts," as I said above, " can only be probable." However solidly founded a predic tion may appear to be, we are never absolutely certain that experiment will not prove it false; but the probability is often so great that practically it may be accepted. And a little farther on I added: — "See what a part the belief in simplicity plays in our generalisations. We have verified a simple law in a large number of particular cases, and we refuse to admit that this so-often-repeated coincidence is a mere effect of chance." Thus, in a multitude of circumstances the physicist is often in the same position as the gambler who reckons up his chances. Every time that he reasons by induction, he more or less consciously requires the calculus of probabilities, and that is why I am obliged to open this chapter parenthetically, and to interrupt our discussion of method in the physical sciences in order to examine a little closer what this calculus is worth, and what dependence we may place upon it. The very name of the calculus of probabilities is a paradox. Probability as opposed to certainty is what one does not know, and how can we calculate the unknown ? Yet many eminent scientists have devoted themselves to this calculus, and it cannot be denied that science has drawn there from no small advantage. How can we explain this apparent contradiction ? Has probability been defined ? Can it even be defined ? And if it can not, how can we venture to reason upon it ? The definition, it will be said, is very simple. The probability of an event is the ratio of the number of cases favourable to the event to the total number of possible cases. A simple example will show how incomplete this definition is: — I throw two dice. What is the probability that one of the two at least turns up a 6 ? Each can turn up in six different ways; the number of possible cases is 6 x 6 = 36. The number of favourable cases is n ; the probability is -1- That is the correct solution. But why cannot we just as well proceed as follows? -The points which turn up on the two dice form — = 2 1 different combinations. Among these combinations, six are favourable ; the probability THE CALCULUS OF PROBABILITIES. 185 is — • Now why is the first method of calculating the number of possible cases more legitimate than the second ? In any case it is not the definition that tells us. We are therefore bound to complete the definition by saying, " ... to the total number of possible cases, provided the cases are equally probable." So we are compelled to define the probable by the probable. How can we know that two possible cases are equally probable ? Will it be by a convention ? If we insert at the beginning of every problem an explicit convention, well and good ! We then have nothing to do but to apply the rules of arithmetic and algebra, and we complete our calculation, when our result cannot be called in question. But if we wish to make the slightest application of this result, we must prove that our convention is legitimate, and we shall find ourselves in the presence of the very difficulty we thought we had avoided. It may be said that common-sense is enough to show us the convention that should be adopted. Alas ! M. Bertrand has amused himself by discussing the following simple problem : — " What is the probability that a chord of a circle may be greater than the side of the inscribed equilateral triangle?" The illustrious geometer successively adopted two conventions which seemed to be equally imperative in the eyes of common-sense, and with one convention he finds J, and with the other J-. The conclusion which seems to follow- from this is that the calculus of probabilities is a useless science, that the obscure instinct which we call common-sense, and to which we appeal for the legitimisation of our conventions, must be distrusted. But to this conclusion we can no longer subscribe. We cannot do without that obscure instinct. Without it, science would be impossible, and without it we could neither discover nor apply a law. Have we any right, for instance, to enunciate Newton's law ? No doubt numerous observations are in agreement with it, but is not that a simple fact of chance ? and how do we know, besides, that this law which has been true for so many generations will not be untrue in the next ? To this objection the only answer you can give is: It is very improbable. But grant the law. By means of it I can calculate the position of Jupiter in a year from now. Yet have I any right to say this? Who can tell if a gigantic mass of enormous velocity is not going to pass near the solar system and produce unforeseen perturbations ? Here again the only answer is : It is very improbable. From this point of view all the sciences would only be unconscious applications of the calculus of prob abilities. And if this calculus be condemned, then the whole of the sciences must also be condemned. I shall not dwell at length on scientific problems in which the intervention of the calculus of prob abilities is more evident. In the forefront of these is the problem of interpolation, in which, knowing a certain number of values of a function, we try to discover the intermediary values. I may also mention the celebrated theory of errors of observa- THE CALCULUS OF PROBABILITIES. 187 tion, to which I shall return later; the kinetic theory of gases, a well-known hypothesis wherein each gaseous molecule is supposed to describe an extremely complicated path, but in which, through the effect of great numbers, the mean phenomena \vhich are all we observe obey the simple laws of Mariotte and Gay-Lussac. All these theories are based upon the laws of great numbers, and the calculus of probabilities would evidently involve them in its ruin. It is true that they have only a particular interest, and that, save as far as inter polation is concerned, they are sacrifices to which we might readily be resigned. But I have said above, it would not be these partial sacrifices that would be in question ; it would be the legitimacy of the whole of science that would be challenged. I quite see that it might be said: We do not know, and yet we must act. As for action, we have not time to devote ourselves to an inquiry that will suffice to dispel our ignorance. Besides, such an inquiry would demand unlimited time. We must therefore make up our minds without knowing. This must be often done whatever may happen, and we must follow the rules although we may have but little confidence in them. What I know is, not that such a thing is true, but that the best course for me is to act as if it were true. The calculus of probabilities, and therefore science itself, would be no longer of any practical value. Unfortunately the difficulty does not thus dis appear. A gambler wants to try a coup, and he asks my advice. If I give it him, I use the calculus of probabilities; but I shall not guarantee success. That is what I shall call subjective prob ability. In this case we might be content with the explanation 'of which I have just given a sketch. But assume that an observer is present at the play, that he knows of the coup, and that play goes on for a long time, and that he makes a summary of his notes. He will find that events have taken place in conformity with the laws of the calculus of probabilities. That is what I shall call objective probability, and it is this phenomenon which has to be explained. There are numerous Insurance Societies which apply the rules of the calculus of probabilities, and they distribute to their shareholders dividends, the objective reality of which cannot be contested. In order to explain them, we must do more than invoke our ignorance and the necessity of action. Thus, absolute scepti cism is not admissible. We may distrust, but we cannot condemn en bloc. Discussion is necessary. I. Classification of the Problems of Probability. — In order to classify the problems which are presented to us with reference to probabilities, we must look at them from different points of view, and first of all, from that of generality. I said above that prob ability is the ratio of the number of favourable to the number of possible cases. What for want of a better term I call generality will increase with the number of possible cases. This number may be finite, as, for instance, if we take a throw of the THE CALCULUS OF PROBABILITIES. l8g dice in which the number of possible cases is 36. That is the first degree of generality. But if we ask, for instance, what is the probability that a point within a circle is within the inscribed square, there are as many possible cases as there are points in the circle — that is to say, an infinite number. This is the second degree of generality. Generality can be pushed further still. We may ask the prob ability that a function will satisfy a given condi tion. There are then as many possible cases as one can imagine different functions. This is the third degree of generality, which we reach, for instance, wrhen we try to find the most probable law after a finite number of observations. Yet we may place ourselves at a quite different point of view. If we were not ignorant there would be no probability, there could only be certainty. But our ignorance cannot be absolute, for then there would be no longer any probability at all. Thus the problems of probability may be classed according to the greater or less depth of this ignorance. In mathe matics we may set ourselves problems in prob ability. What is the probability that the fifth decimal of a logarithm taken at random from a table is a 9. There is no hesitation in answering that this probability is i-ioth. Here we possess all the data of the problem. We can calculate our logarithm without having recourse to the table, but we need not give ourselves the trouble. This . is the first degree of ignorance. In the physical sciences our ignorance is already greater. The state of a system at a given moment depends on two things — its initial state, and the law according to which that state varies. If we know both this lawr and this initial state, we have a simple mathematical problem to solve, and we fall back upon our first degree of ignorance. Then it often happens that we know the law and do not know the initial state. It may be asked, for instance, what is the present distribu tion of the minor planets ? We know that from all time they have obeyed the laws of Kepler, but we do not know what was their initial dis tribution. In the kinetic theory of gases we assume that the gaseous molecules follow recti linear paths and obey the laws of impact and elastic bodies; yet as we know nothing of their initial velocities, we know nothing of their present velocities. The calculus of probabilities alone enables us to predict the mean phenomena which will result from a combination of these velocities. This is the second degree of ignorance. Finally it is possible, that not only the initial conditions but the laws themselves are unknown. We then reach the third degree of ignorance, and in general we can no longer affirm anything at all as to the probability of a phenomenon. It often happens that instead of trying to discover an event by means of a more or less imperfect knowledge of the law, the events may be known, and we want to find the law ; or that, instead of deducing effects from causes, we wish to deduce the causes THE CALCULUS OF PROBABILITIES. IQI from the effects. Now, these problems are classified as probability of causes, and are the most interesting of all from their scientific applications. I play at ecarte with a gentleman whom I know to be per fectly honest. What is the chance that he turns up the king ? It is -J-. This is a problem of the probability of effects. I play with a gentleman whom I do not know. He has dealt ten times, and he has turned the king up six times. What is the chance that he is a sharper ? This is a problem in the probability of causes. It may be said that it is the essential problem of the experi mental method. I have observed n values of x and the corresponding values of y. I have found that the ratio of the latter to the former is prac tically constant. There is the event ; what is the cause ? Is it probable that there is a general law according to which y would be proportional to x, and that small divergencies are due to errors of observation ? This is the type of question that we are ever asking, and which we unconsciously solve whenever we are engaged in scientific work. I am now going to pass in review these different categories of problems by discussing in succession what I have called subjective and objective prob ability. II. Probability in Mathematics. — The impossi bility of squaring the circle was shown in 1885, but before that date all geometers considered this im possibility as so " probable" that the Academic des Sciences rejected without examination the, alas ! too numerous memoirs on this subject that a few unhappy madmen sent in every year. Was the Academic wrong ? Evidently not, and it knew perfectly well that by acting in this manner it did not run the least risk of stifling a discovery of moment. The Academic could not have proved that it was right, but it knew quite well that its instinct did not deceive it. If you had asked the Academicians, they would have answered: "We have compared the prob ability that an unknown scientist should have found out what has been vainly sought for so long, with the probability that there is one mad man the more on the earth, and the latter has appeared to us the greater." These are very good reasons, but there is nothing mathematical about them; they are purely psychological. If you had pressed them further, they would have added: " Why do you expect a particular value of a transcendental function to be an algebraical number; if ^ be the root of an algebraical equa tion, why do you expect this root to be a period of the function sin 2x, and why is it not the same with the other roots of the same equation?" To sum up, they would have invoked the principle of sufficient reason in its vaguest form. Yet what information could they draw from it ? At most a rule of conduct for the employment of their time, which would be more usefully spent at their ordinary work than in reading a lucubration that inspired in them a legitimate distrust. But THE CALCULUS OF PROBABILITIES. IQ3 what I called above objective probability has nothing in common with this first problem. It is otherwise with the second. Let us consider the first 10,000 logarithms that we find in a table. Among these 10,000 logarithms I take one at random. What is the probability that its third decimal is an even number ? You will say with out any hesitation that the probability is J, and in fact if you pick out in a table the third decimals in these 10,000 numbers you will find nearly as many even digits as odd. Or, if you prefer it, let us write 10,000 numbers corresponding to our 10,000 logarithms, writing down for each of these numbers 4- 1 if the third decimal of the correspond ing logarithm is even, and - i if odd; and then let us take the mean of these 10,000 numbers. I do not hesitate to say that the mean of these 10,000 units is probably zero, and if I were to calculate it practically, I would verify that it is extremely small. But this verification is needless. I might have rigorously proved that this mean is smaller than 0.003. To prove this result I should have had to make a rather long calculation for which there is no room here, and for which I may refer the reader to an article that I pub lished in the Revue generate des Sciences, April I5th, 1899. The only point to which I wish to draw attention is the following. In this calcula tion I had occasion to rest my case on only two facts — namely, that the first and second derivatives of the logarithm remain, in the interval considered, between certain limits. Hence our first conclusion is that the property is not only true of the logarithm but of any continuous function what ever, since the derivatives of every continuous function are limited. If I was certain beforehand of the result, it is because I have often observed analogous facts for other continuous functions; and next, it is because I went through in my mind in a more or less unconscious and imperfect manner the reasoning which led me to the preceding in equalities, just as a skilled calculator before finish ing his multiplication takes into account what it ought to come to approximately. And besides, since what I call my intuition was only an incom plete summary of a piece of true reasoning, it is clear that observation has confirmed my predic tions, and that the objective and subjective proba bilities are in agreement. As a third example I shall choose the following: — The number u is taken at random and n is a given very large integer. What is the mean value of sin mi ? This problem has no meaning by itself. To give it one, a convention is required — namely, we agree that the probability for the number u to lie between a and a + da is (a)da; that it is therefore proportional to the infinitely small interval da, and is equal to this multiplied by a function (/i), only depending on a. As for this function I choose it arbitrarily, but I must assume it to be continuous. The value of sin nu remaining the same when u increases by 2 TT, I may without loss of generality assume that THE CALCULUS OF PROBABILITIES. 195 u lies between o and 2 TT, and I shall thus be led to suppose that (a) is a periodic function whose period is 2 TT. The mean value that we seek is readily expressed by a simple integral, and it is easy to show that this integral is smaller than —^, MK being the maximum value of the Kth derivative of (f>(u). We see then that if the Kth derivative is finite, our mean value will tend towards zero when n increases indefinitely, and that more rapidly than -— . The mean r j w>-i value of sin nu when n is very large is therefore zero. To define this value I required a conven tion, but the result remains the same whatever that convention may be. I have imposed upon myself but slight restrictions when I assumed that the function (j>(a) is continuous and periodic, and these hypotheses are so natural that we may ask ourselves how they can be escaped. Examination of the three preceding examples, so different in all respects, has already given us a glimpse on the one hand of the role of what philosophers call the principle of sufficient reason, and on the other hand of the importance of the fact that certain pro perties are common to all continuous functions. The study of probability in the physical sciences will lead us to the same result. III. Probability in the Physical Sciences. — We now come to the problems which are connected with what I have called the second degree of ignorance — namely, those in which we know the law but do not know the initial state of the system. I could multiply examples, but I shall take only one. What is the probable present distribution of the minor planets on the zodiac ? We know they obey the laws of Kepler. We may even, without changing the nature of the problem, suppose that their orbits are circular and situated in the same plane, a plane which we are given. On the other hand, we know absolutely nothing about their initial distribution. However, we do not hesitate to affirm that this distribution is now nearly uniform. Why? Let b be the longitude of a minor planet in the initial epoch — that is to say, the epoch zero. Let a be its mean motion. Its longitude at the present time — i.e., at the time / will be at + b. To say that the present distribu tion is uniform is to say that the mean value of the sines and cosines of multiples of at + b is zero. Why do we assert this ? Let us represent our minor planet by a point in a plane — namely, the point whose co-ordinates are a and b. All these representative points will be contained in a certain region of the plane, but as they are very numerous this region will appear dotted with points. We know nothing else about the distribution of the points. Now what do we do when we apply the calculus of probabilities to such a question as this ? What is the probability that one or more representative points may be found in a certain portion of the plane ? In our ignorance we are THE CALCULUS OF PROBABILITIES. IQ7 compelled to make an arbitrary hypothesis. To explain the nature of this hypothesis I may be allowed to use, instead of a mathematical formula, a crude but concrete image. Let us suppose that over the surface of our plane has been spread imaginary matter, the density of which is variable, but varies continuously. We shall then agree to say that the probable number of repre sentative points to be found on a certain portion of the plane is proportional to the quantity of this imaginary matter which is found there. If there are, then, two regions of the plane of the same extent, the probabilities that a representative point of one of our minor planets is in one or other of these regions will be as the mean densities of the imaginary matter in one or other of the regions. Here then are two distributions, one real, in which the representative points are very numerous, very close together, but discrete like the molecules of matter in the atomic hypothesis; the other remote from reality, in which our representa tive points are replaced by imaginary continuous matter. We know that the latter cannot be real, but we are forced to adopt it through our ignorance. If, again, we had some idea of the real distribution of the representative points, we could arrange it so that in a region of some extent the density of this imaginary continuous matter may be nearly pro portional to the number of representative points, or, if it is preferred, to the number of atoms which are contained in that region. Even that is impossible, and our ignorance is so great that we are forced to choose arbitrarily the function which defines the density of our imaginary matter. We shall be compelled to adopt a hypothesis from which we can hardly get away ; we shall sup pose that this function is continuous. That is sufficient, as we shall see, to enable us to reach our conclusion. What is at the instant t the probable distribu tion of the minor planets — or rather, what is the mean value of the sine of the longitude at the moment t — i.e., of sin (at + b)? We made at the outset an arbitrary convention, but if we adopt it, this probable value is entirely defined. Let us decompose the plane into elements of surface. Consider the value of sin (at + b) at the centre of each of these elements. Multiply this value by the surface of the element and by the corresponding density of the imaginary matter. Let us then take the sum for all the elements of the plane. This sum, by definition, will be the probable mean value we seek, which will thus be expressed by a double integral. It may be thought at first that this mean value depends on the choice of the function <£ which defines the density of the imagin ary matter, and as this function is arbitrary, we can, according to the arbitrary choice which we make, obtain a certain mean value. But this is not the case. A simple calculation shows us that our double integral decreases very rapidly as t increases. Thus, I cannot tell what hypothesis to THE CALCULUS OF PROBABILITIES. make as to the probability of this or that initial distribution, but when once the hypothesis is made the result will be the same, and this gets me out of my difficulty. Whatever the function may be, the mean value tends towards zero as t increases, and as the minor planets have certainly accomplished a very large number of revolutions, I may assert that this mean value is very small. I may give to any value I choose, with one restriction : this function must be con tinuous; and, in fact, from the point of view of subjective probability, the choice of a discontinuous function would have been unreasonable. What reason could I have, for instance, for supposing that the initial longitude might be exactly o°, but that it could not lie between o° and i° ? The difficulty reappears if we look at it from the point of view of objective probability; if we pass from our imaginary distribution in which the sup posititious matter was assumed to be continuous, to the real distribution in which our representative points are formed as discrete atoms. The mean value of sin (at + b) will be represented quite simply by \ £ sin (at + b), n being the number of minor planets. Instead of a double integral referring to a continuous function, we shall have a sum of discrete terms. However, no one will seriously doubt that this mean value is practically very small. Our representative points being very close together, our discrete sum will in general differ very little from an integral. An integral is the limit towards which a sum of terms tends when the number of these terms is indefinitely increased. If the terms are very numerous, the sum will differ very little from its limit — that is to say, from the integral, and what I said of the latter will still be true of the sum itself. But there are exceptions. If, for instance, for all the minor planets b = - -at, the longitude of all the planets at the time t would be — , and the mean value in question would be evidently unity. For this to be the case at the time o, the minor planets must have all been lying on a kind of spiral of peculiar form, with its spires very close together. All will admit that such an initial distribution is extremely im probable (and even if it were realised, the distribu tion would not be uniform at the present time — for example, on the ist January 1900 ; but it would become so a few years later). Why, then, do we think this initial distribution improbable ? This must be explained, for if we are wrong in rejecting as improbable this absurd hypothesis, our inquiry breaks down, and we can no longer affirm any thing on the subject of the probability of this or that present distribution. Once more we shall invoke the principle of sufficient reason, to which we must always recur. We might admit that at the beginning the planets were distributed almost THE CALCULUS OF PROBABILITIES. 201 in a straight line. We might admit that they were irregularly distributed. But it seems to us that there is no sufficient reason for the unknown cause that gave them birth to have acted along a curve so regular and yet so complicated, which would appear to have been expressly chosen so that the distribution at the present day would not be uniform. IV. Rouge ct Noir. — The questions raised by games of chance, such as roulette, are, funda mentally, quite analogous to those we have just treated. For example, a wheel is divided into thirtyseven equal compartments, alternately red and black. A ball is spun round the wheel, and after having moved round a number of times, it stops in front of one of these sub-divisions. The probability that the division is red is obviously ^. The needle describes an angle 0, including several complete revolutions. I do not know what is the prob ability that the ball is spun with such a force that this angle should lie between 0 and & + (!&, but I can make a convention. I can suppose that this probability is (6)dQ. As for the function (#), I can choose it in an entirely arbitrary manner. I have nothing to guide me in my choice, but I am naturally induced to suppose the function to be continuous. Let e be a length (measured on the circumference of the circle of radius unity) of each red and black compartment. We have to calcu late the integral of ^(0)dB, extending it on the one hand to all the red, and on the other hand to all • the black compartments, and to compare the results. Consider an interval 2 e comprising two consecutive red and black compartments. Let M and in be the maximum and minimum values of the function (#) in this interval. The integral extended to the red compartments will be smaller than Z Me; extended to the black it will be greater than Z inc. The difference will therefore be smaller than 21 (M - m) e . But if the function 4> is supposed continuous, and if on the other hand the interval c is very small with respect to the total angle described by the needle, the difference M -m will be very small. The difference of the two integrals will be therefore very small, and the probability will be very nearly J. We see that without knowing anything of the function we must act as if the probability were J. And on the other hand it explains why, from the objective point of view, if I watch a certain number of coups, observation will give me almost as many black coups as red. All the players know this objective law; but it leads them into a remarkable error, which has often been exposed, but into which they are always falling. When the red has won, for example, six times running, they bet on black, thinking that they are playing an absolutely safe game, because they say it is a very rare thing for the red to win seven times running. In reality their probability of winning is still ^. Observation shows, it is true, that the series of seven consecutive reds is very rare, THE CALCULUS OF PROBABILITIES. 203 but series of six reds followed by a black are also very rare. They have noticed the rarity of the series of seven reds; if they have not remarked the rarity of six reds and a black, it is only because such series strike the attention less. V. The Probability of Causes.- — We now come to the problems of the probability of causes, the most important from the point of view of scientific applications. Two stars, for instance, are very close together on the celestial sphere. Is this apparent contiguity a mere effect of chance ? Are these stars, although almost on the same visual ray, situated at very different distances from the earth, and therefore very far indeed from one another ? or does the apparent correspond to a real contiguity ? This is a problem on the probability of causes. First of all, I recall that at the outset of all problems of probability of effects that have occupied our attention up to now, we have had to use a convention which was more or less justified; and if in most cases the result was to a certain extent independent of this convention, it was only the condition of certain hypotheses which enabled us a priori to reject discontinuous functions, 'for example, or certain absurd con ventions. We shall again find something analogous to this when we deal with the prob ability of causes. An effect may be produced by the cause a or by the cause b. The effect has just been observed. We ask the probability that it is due to the cause a. This is an a posteriori probability of cause. But I could not calculate it, if a convention more or less justified did not tell me in advance what is the a priori probability for the cause a to come into play — I mean the probability of this event to some one who had not observed the effect. To make my meaning clearer, I go back to the game of ecarte mentioned before. My adversary deals for the first time and turns up a king. What is the probability that he is a sharper ? The formulae ordinarily taught give -J, a result which is obviously rather surprising. If we look at it closer, we see that the conclusion is arrived at as if, before sitting down at the table, I had considered that there was one chance in two that my adversary was not honest. An absurd hypothesis, because in that case I should certainly not have played with him ; and this explains the absurdity of the conclusion. The function on the a priori probability was unjustified, and that is why the conclusion of the a posteriori probability led me into an inadmissible result. The import ance of this preliminary convention is obvious. I shall even add that if none were made, the problem of the a posteriori probability would have no meaning. It -must be always made either explicitly or tacitly. Let us pass on to an example of a more scientific character. I require to determine an experimental law; this law, when discovered, can THE CALCULUS OF PROBABILITIES. 205 be represented by a curve. I make a certain number of isolated observations, each of which may be represented by a point. When I have obtained these different points, I draw a curve between them as carefully as possible, giving my curve a regular form, avoiding sharp angles, accentuated inflexions, and any sudden variation of the radius of curvature. This curve will repre sent to me the probable law, and not only will it give me the values of the functions intermediary to those which have been observed, but it also gives me the observed values more accurately than direct observation does; that is why I make the curve pass near the points and not through the points themselves. Here, then, is a problem in the probability of causes. The effects are the measurements I have recorded; they depend on the combination of twro causes — the true law of the phenomenon and errors of observation. Knowing the effects, we have to find the probability that the phenomenon shall obey this law or that, and that the observations have been accompanied by this or that error. The most probable law, therefore, corresponds to the curve we have traced, and the most probable error is represented by the distance of the cor responding point from that curve. But the problem has no meaning if before the observa tions I had an a priori idea of the probability of this law or that, or of the chances of error to which I am exposed. If my instruments are good (and I knew whether this is so or not before beginning the observations), I shall not draw the curve far from the points which represent the rough measurements. If they are inferior, I may draw it a little farther from the points, so that I may get a less sinuous curve; much will be sacri ficed to regularity. Why, then, do I draw a curve without sinu osities ? Because I consider a priori a law represented by a continuous function (or function the derivatives of which to a high order are small), as more probable than a law not satisfying those conditions. But for this conviction the problem would have no meaning ; interpolation would be impossible; no law could be deduced from a finite number of observations ; science would cease to exist. Fifty years ago physicists considered, other things being equal, a simple law as more probable than a complicated law. This principle was even invoked in favour of Mariotte's law as against that of Regnault. But this belief is now repudiated ; and yet, how many times are we compelled to act as though we still held it! However that may be, what remains of this tendency is the belief in continuity, and as we have just seen, if the belief in continuity were to disappear, experimental science would become impossible. VI. The Theory of Errors. — We are thus brought to consider the theory of errors which is directly THE CALCULUS OF PROBABILITIES. 207 connected with the problem of the probability of causes. Here again we find effects — to wit, a certain number of irreconcilable observations, and we try to find the causes which are, on the one hand, the true value of the quantity to be measured, and, on the other, the error made in each isolated observation. We must calculate the probable a posteriori value of each error, and therefore the probable value of the quantity to be measured. But, as I have just explained, we cannot undertake this calculation unless we admit a priori — i.e., before any observations are made — that there is a law of the probability of errors. Is there a law of errors ? The law to which all calculators assent is Gauss's law, that is represented by a certain transcendental curve known as the " bell." But it is first of all necessary to recall the classic distinction between systematic and accidental errors. If the metre with which we measure a length is too long, the number we get will be too small, and it will be no use to measure several times — that is a systematic error. If we measure with an accurate metre, we may make a mistake, and find the length sometimes too large and sometimes too small, and when we take the mean of a large number of measurements, the error will tend to grow small. These are accidental errors. It is clear that systematic errors do not satisfy Gauss's law, but do accidental errors satisfy it ? Numerous proofs have been attempted, almost all of them crude paralogisms. But starting from the following hypotheses we may prove Gauss's law : the error is the result of a very large number of partial and independent errors ; each partial error is very small and obeys any law of prob ability whatever, provided the probability of a positive error is the same as that of an equal negative error. It is clear that these conditions will be often, but not always, fulfilled, and we may reserve the name of accidental for errors which satisfy them. We see that the method of least squares is not legitimate in every case ; in general, physicists are more distrustful of it than astronomers. This is no doubt because the latter, apart from the systematic errors to which they and the physicists are subject alike, have to contend with an extremely important source of error which is entirely accidental — I mean atmospheric undula tions. So it is very curious to hear a discussion between a physicist and an astronomer about a method of observation. The physicist, persuaded that one good measurement is wrorth more than many bad ones, is pre-eminently concerned with the elimination by means of every precaution of the final systematic errors; the astronomer retorts : " But you can only observe a small number of stars, and accidental errors will not disappear." What conclusion must we draw7 ? Must we continue to use the method of least squares ? THE CALCULUS OF PROBABILITIES. 20Q We must distinguish. We have eliminated all the systematic errors of which we have any suspicion ; we are quite certain that there are others still, but we cannot detect them ; and yet we must make up our minds and adopt a definitive value which will be regarded as the probable value ; and for that purpose it is clear that the best thing we can do is to apply Gauss's law. We have only applied a practical rule referring to subjective probability. And there is no more to be said. Yet we want to go farther and say that not only the probable value is so much, but that the probable error in the result is so much. This is absolutely invalid : it would be true only if we were sure that all the systematic errors were eliminated, and of that we know absolutely nothing. We have two series of observations; by applying the law of least squares we find that the probable error in the first series is twice as small as in the second. The second series may, how ever, be more accurate than the first, because the first is perhaps affected by a large systematic error. All that we can say is, that the first series is probably better than the second because its accidental error is smaller, and that we have no reason for affirming that the systematic error is greater for one of the series than for the other, our ignorance on this point being absolute. VII. Conclusions. — In the preceding lines I have set several problems, and have given no solution. I do not regret this, for perhaps they will invite the reader to reflect on these delicate questions. However that may be, there are certain points which seem to be well established. To undertake the calculation of any probability, and even for that calculation to have any meaning at all, we must admit, as a point of departure, an hypothesis or convention which has always something arbitrary about it. In the choice of this con vention we can be guided only by the principle of sufficient reason. Unfortunately, this principle is very vague and very elastic, and in the cursory examination we have just made we have seen it assume different forms. The form under which we meet it most often is the belief in continuity, a belief which it would be difficult to justify by apodeictic reasoning, but without which all science would be impossible. Finally, the problems to which the calculus of probabilities may be applied with profit are those in which the result is inde pendent of the hypothesis made at the outset, provided only that this hypothesis satisfies the condition of continuity. CHAPTER XII.1 OPTICS AND ELECTRICITY. FresneVs Theory. — The best example that can be chosen is the theory of light and its relations to the theory of electricity. It is owing to Fresnel that the science of optics is more advanced than any other branch of physics. The theory called the theory of undulations forms a complete whole, which is satisfying to the mind ; but we must not ask from it what it cannot give us. The object of mathematical theories is not to reveal to us the real nature of things; that would be an unreasonable claim. Their only object is to co-ordinate the physical laws with which physical experiment makes us acquainted, the enunciation of which, without the aid of mathematics, we should be unable to effect. Whether the ether exists or not matters little — let us leave that to the metaphysicians; what is essential for us is, that everything happens as if it existed, and that this hypothesis is found to be suitable for the explana tion of phenomena. After all, have we any other 1 This chapter is mainly taken from the prefaces of two of my books^— Theorie Mathematique de la lumiere (Paris: Naud, 1889), and Electricite et Optique (Paris: Naud, 1901). reason for believing in the existence of material objects? That, too, is only a convenient hypothesis ; only, it will never cease to be so, while some day, no doubt, the ether will be thrown aside as useless. But at the present moment the laws of optics, and the equations which translate them into the language of analysis, hold good — at least as a first approximation. It will therefore be always useful to study a theory which brings these equations into connection. The undulatory theory is based on a molecular hypothesis ; this is an advantage to those who think they can discover the cause under the law. But others find in it a reason for distrust ; and this distrust seems to me as unfounded as the illusions of the former. These hypotheses play but a secondary role. They may be sacrificed, and the sole reason why this is not generally done is, that it would involve a certain loss of lucidity in the explanation. In fact, if we look at it a little closer we shall see that we borrow from molecular hypotheses but two things — the principle of the conservation of energy, and the linear form of the equations, which is the general law of small movements as of all small variations. This ex plains why most of the conclusions of Fresnel remain unchanged when we adopt the electro magnetic theory of light. Maxwell's Theory. — We all know that it was Maxwell who connected by a slender tie two branches of physics — optics and electricity — until OPTICS AND ELECTRICITY. 213 then unsuspected of having anything in common. Thus blended in a larger aggregate, in a higher harmony, Fresnel's theory of optics did not perish. Parts of it are yet alive, and their mutual relations are still the same. Only, the language which we use to express them has changed ; and, on the other hand, Maxwell has revealed to us other relations, hitherto unsuspected, between the different branches of optics and the domain of electricity. The first time a French reader opens Maxwell's book, his admiration is tempered with a feeling of uneasiness, and often of distrust. It is only after prolonged study, and at the cost of much effort, that this feeling disappears. Some minds of high calibre never lose this feeling. Why is it so difficult for the ideas of this English scientist to become acclimatised among us? No doubt the education received by most enlightened Frenchmen predisposes them to appreciate pre cision and logic more than any other qualities. In this respect the old theories of mathematical physics gave us complete satisfaction. All our masters, from Laplace to Cauchy, proceeded along the same lines. Starting with clearly enunciated hypotheses, they deduced from them all their consequences with mathematical rigour, and then compared them with experiment. It seemed to be their aim to give to each of the branches of physics the same precision as to celestial mechanics. A mind accustomed to admire such models is not easily satisfied with a theory. Not only will it not tolerate the least appearance of contradic tion, but it will expect the different parts to be logically connected with one another, and will require the number of hypotheses to be reduced to a minimum. This is not all ; there will be other demands which appear to me to be less reasonable. Behind the matter of which our senses are aware, and which is made known to us by experiment, such a thinker will expect to see another kind of matter —the only true matter in its opinion — which will no longer have anything but purely geometrical qualities, and the atoms of which will be mathe matical points subject to the laws of dynamics alone. And yet he will try to represent to himself, by an unconscious contradiction, these invisible and colourless atoms, and therefore to bring them as close as possible to ordinary matter. Then only will he be thoroughly satisfied, and he will then imagine that he has penetrated the secret of the universe. Even if the satisfaction is fallacious, it is none the less difficult to give it up. Thus, on opening the pages of Maxwell, a French man expects to find a theoretical whole, as logical and as precise as the physical optics that is founded on the hypothesis of the ether. He is thus pre paring for himself a disappointment which I should like the reader to avoid ; so I will warn OPTICS AND ELECTRICITY. 215 him at once of what he will find and what he will not find in Maxwell. Maxwell does not give a mechanical explanation of electricity and magnetism ; he confines himself to showing that such an explanation is possible, He shows that the phenomena of optics are only a particular case of electro-magnetic phenomena. From the whole theory of electricity a theory of light can be immediately deduced. Unfortunately the converse is not true ; it is not always easy to find a complete. explanation of electrical pheno mena. In particular it is not easy if we take as our starting-point Fresnel's theory; to do so, no doubt, would be impossible; but none the less we must ask ourselves if we are compelled to surrender admirable results which we thought we had definitively acquired. That seems a step backwards, and many sound intellects will not willingly allow of this. Should the reader consent to set some bounds to his hopes, he will still come across other difficulties. The English scientist does not try to erect a unique, definitive, and well-arranged building; he seems to raise rather a large number of provisional and independent constructions, between which communication is difficult and sometimes impossible. Take, for instance, the chapter in which electrostatic attractions are explained by the pressures and tensions of the dielectric medium. This chapter might be sup pressed without the rest of the book being thereby less clear or less complete, and yet it contains a theory which is self-sufficient, and which can be understood without reading a word of what precedes or follows. But it is not only independent of the rest of the book ; it is difficult to reconcile it with the fundamental ideas of the volume. Maxwell does not even attempt to reconcile it; he merely says: "I have not been able to make the next step — namely, to account by mechanical considerations for these stresses in the dielectric." This example will be sufficient to show wrhat I mean ; I could quote many others. Thus, who would suspect on reading the pages devoted to magnetic rotatory polarisation that there is an identity between optical and magnetic pheno mena ? We must not flatter ourselves that we have avoided every contradiction, but we ought to make up our minds. Two contradictory theories, provided that they are kept from overlapping, and that we do not look to find in them the explana tion of things, may, in fact, be very useful instru ments of research ; and perhaps the reading of Maxwell would be less suggestive if he had not opened up to us so many new and divergent ways. But the fundamental idea is masked, as it were. So far is this the case, that in most works that are popularised, this idea is the only point which is left completely untouched. To show the import ance of this, I think I ought to explain in what this OPTICS AND ELECTRICITY. 217 fundamental idea consists ; but for that purpose a short digression is necessary. The Mechanical Explanation of Physical Phenomena. —In every physical phenomenon there is a certain number of parameters which are reached directly by experiment, and which can be measured. I shall call them the parameters q. Observation next teaches us the laws of the variations of these parameters, and these laws can be generally stated in the form of differential equations which connect together the parameters q and time. What can be done to give a mechanical interpretation to such a phenomenon ? We may endeavour to explain it, either by the movements of ordinary matter, or by those of one or more hypothetical fluids. These fluids will be considered as formed of a very large number of isolated molecules m. When may we say that we have a complete mechanical explanation of the phenomenon? It will be, on the one hand, when we know the differential equations which are satisfied by the co-ordinates of these hypothetical molecules /;/, equations which must, in addition, conform to the laws of dynamics; and, on the other hand, when we know the relations which define the co-ordinates of the molecules m as functions of the parameters q, attainable by experiment. These equations, as I have said, should conform to the principles of dynamics, and, in particular, to the principle of the conservation of energy, and to that of least action. The first of these two principles teaches us that the total energy is constant, and may be divided into two parts : (i) Kinetic energy, or vis viva, which depends on the masses of the hypothetical molecules m, and on their velocities. This I shall call T. (2) The potential energy which depends only on the co-ordinates of these molecules, and this I shall call U. It is the sum of the energies T and U that is constant. Now what are we taught by the principle of least action ? It teaches us that to pass from the initial position occupied at the instant to to the final position occupied at the instant tlf the system must describe such a path that in the interval of time between the instant to and tv the mean value of the action — i.e., the difference between the two energies T and U, must be as small as possible. The first of these two principles is, moreover, a consequence of the second. If we know the functions T and U, this second principle is sufficient to determine the equations of motion. Among the paths which enable us to pass from one position to another, there is clearly one for which the mean value of the action is smaller than for all the others. In addition, there is only^such path ; and it follows from this, that the principle of least action is sufficient to determine the path followed, and therefore the equations of motion. We thus obtain what are called the equations of Lagrange. In these equations the independent OPTICS AND ELECTRICITY. 2IQ variables are the co-ordinates of the hypothetical molecules m; but I now assume that we take for the variables the parameters q, which are directly accessible to experiment. The two parts of the energy should then be expressed as a function of the parameters q and their derivatives ; it is clear that it is under this form that they will appear to the experimenter. The latter will naturally endeavour to define kinetic and potential energy by the aid of quantities he can directly observe.1 If this be granted, the system will always proceed from one position to another by such a path that the mean value of the action is a minimum. It matters little that T and U are now expressed by the aid of the parameters q and their derivatives ; it matters little that it is also by the aid of these parameters that we define the initial and fina positions; the principle of least action will always remain true. Now here again, of the whole of the paths which lead from one position to another, there is one and only one for which the mean action is a minimum. The principle of least action is therefore sufficient for the determination of the differential equations which define the variations of the parameters q. The equations thus obtained are another form of Lagrange's equations. 1 We may add that U will depend only on the q parameters, that T will depend on them and their derivatives with respect to time, and will be a homogeneous polynomial of the second degree with respect to these derivatives. To form these equations we need not know the relations which connect the parameters q with the co-ordinates of the hypothetical molecules, nor the masses of the molecules, nor the expression of U as a function of the co-ordinates of these molecules. All we need know is the expression of U as a function of the parameters q, and that of T as a function of the parameters q and their derivatives — i.e., the expressions of the kinetic and potential energy in terms of experimental data. One of two things must now happen. Either for a convenient choice of T and U the Lagrangian equations, constructed as we have indicated, will be identical with the differential equations deduced from experiment, or there will be no functions T and U for which this identity takes place. In the latter case it is clear that no mechanical explana tion is possible. The necessary condition for a mechanical explanation to be possible is therefore this : that we may choose the functions T and U so as to satisfy the principle of least action, and of the conservation of energy. Besides, this condition is sufficient. Suppose, in fact, that we have found a function U of the parameters q, which represents one of the parts of energy, and that the part of the energy which we represent by T is a function of the parameters q and their derivatives; that it is a polynomial of the second degree with respect to its derivatives, and finally that the Lagrangian equations formed by the aid of these two functions T and U are in conformity with the data of the OPTICS AND ELECTRICITY. 221 experiment. How can we deduce from this a mechanical explanation ? U must be regarded as the potential energy of a system of which T is the kinetic energy. There is no difficulty as far as U is concerned, but can T be regarded as the vis viva of a material system ? 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Crown 8vo, about 350 pp. each, Cloth Cover, 2/6 per vol. ; Half- Polished Morocco, Gilt Top, 53. Count Tolstoy's Works. The following Volumes are already issued — AND OTHER A RUSSIAN PROPRIETOR. THE COSSACKS. IVAN ILYITCH, STORIES. MY RELIGION. LIFE. MY CONFESSION. CHILDHOOD, BOYHOOD, YOUTH. THE PHYSIOLOGY OF WAR. WHAT TO DO? THE LONG EXILE, ETC. SEVASTOPOL. THE KREUTZER SONATA, AND FAMILY HAPPINESS. THE KINGDOM OF GOD IS WITHIN YOU. WORK WHILE YE HAVE THE LIGHT. THE GOSPEL IN BRIEF. Uniform with the above — IMPRESSIONS OF RUSSIA. By Dr. GEORG BRANDES. In the "World's Great Novels" Series. Large Crown 8vo, Cloth, Gilt Top, Illustrated, Price 3/6 per vol. WAR AND PEACE. (2 vols.) ANNA KARENINA. Also cheap edition, 2/- net. l/~ Booklets by Count Tolstoy. Bound in White Grained Boards, with Gilt Lettering. WHERE LOVE IS, THERE GOD IS ALSO. THE TWO PILGRIMS. WHAT MEN LIVE BY. THE GODSON. IF YOU NEGLECT THE FIRE, YOU DON'T PUT IT OUT. 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