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I bring together here different studies relating more or less directly to questions of scientific methodology. The scientific method consists in observing and experimenting; if the scientist had at his disposal infinite time, it would only be necessary to say to him: ‘Look and notice well’; but, as there is not time to see everything, and as it is better not to see than to see wrongly, it is necessary for him to make choice. The first question, therefore, is how he should make this choice. This question presents itself as well to the physicist as to the historian; it presents itself equally to the mathematician, and the principles which should guide each are not without analogy. The scientist conforms to them instinctively, and one can, reflecting on these principles, foretell the future of mathematics.

We shall understand them better yet if we observe the scientist at work, and first of all it is necessary to know the psychologic mechanism of invention and, in particular, that of mathematical creation. Observation of the processes of the work of the mathematician is particularly instructive for the psychologist.

In all the sciences of observation account must be taken of the errors due to the imperfections of our senses and our instruments. Luckily, we may assume that, under certain conditions, these errors are in part self-compensating, so as to disappear in the average; this compensation is due to chance. But what is chance? This idea is difficult to justify or even to define; and yet what I have just said about the errors of observation, shows that the scientist can not neglect it. It therefore is necessary to give a definition as precise as possible of this concept, so indispensable yet so illusive.

These are generalities applicable in sum to all the sciences; and for example the mechanism of mathematical invention does not differ sensibly from the mechanism of invention in general. Later I attack questions relating more particularly to certain special sciences and first to pure mathematics.

In the chapters devoted to these, I have to treat subjects a little more abstract. I have first to speak of the notion of space; every one knows space is relative, or rather every one says so, but many think still as if they believed it absolute; it suffices to reflect a little however to perceive to what contradictions they are exposed.

The questions of teaching have their importance, first in themselves, then because reflecting on the best way to make new ideas penetrate virgin minds is at the same time reflecting on how these notions were acquired by our ancestors, and consequently on their true origin, that is to say, in reality on their true nature. Why do children usually understand nothing of the definitions which satisfy scientists? Why is it necessary to give them others? This is the question I set myself in the succeeding chapter and whose solution should, I think, suggest useful reflections to the philosophers occupied with the logic of the sciences.

On the other hand, many geometers believe we can reduce mathematics to the rules of formal logic. Unheard-of efforts have been made to do this; to accomplish it, some have not hesitated, for example, to reverse the historic order of the genesis of our conceptions and to try to explain the finite by the infinite. I believe I have succeeded in showing, for all those who attack the problem unprejudiced, that here there is a fallacious illusion. I hope the reader will understand the importance of the question and pardon me the aridity of the pages devoted to it.

The concluding chapters relative to mechanics and astronomy will be easier to read.

Mechanics seems on the point of undergoing a complete revolution. Ideas which appeared best established are assailed by bold innovators. Certainly it would be premature to decide in their favor at once simply because they are innovators.

But it is of interest to make known their doctrines, and this is what I have tried to do. As far as possible I have followed the historic order; for the new ideas would seem too astonishing unless we saw how they arose.

Astronomy offers us majestic spectacles and raises gigantic problems. We can not dream of applying to them directly the experimental method; our laboratories are too small. But analogy with phenomena these laboratories permit us to attain may nevertheless guide the astronomer. The Milky Way, for example, is an assemblage of suns whose movements seem at first capricious. But may not this assemblage be compared to that of the molecules of a gas, whose properties the kinetic theory of gases has made known to us? It is thus by a roundabout way that the method of the physicist may come to the aid of the astronomer.

Finally I have endeavored to give in a few lines the history of the development of French geodesy; I have shown through what persevering efforts, and often what dangers, the geodesists have procured for us the knowledge we have of the figure of the earth. Is this then a question of method? Yes, without doubt, this history teaches us in fact by what precautions it is necessary to surround a serious scientific operation and how much time and pains it costs to conquer one new decimal.

Science and the Scientist

Tolstoi somewhere explains why ‘science for its own sake’ is in his eyes an absurd conception. We can not know
*all* facts, since their number is practically infinite. It is necessary to choose; then we may let this choice
depend on the pure caprice of our curiosity; would it not be better to let ourselves be guided by utility, by our
practical and above all by our moral needs; have we nothing better to do than to count the number of lady-bugs on our
planet?

It is clear the word utility has not for him the sense men of affairs give it, and following them most of our contemporaries. Little cares he for industrial applications, for the marvels of electricity or of automobilism, which he regards rather as obstacles to moral progress; utility for him is solely what can make man better.

For my part, it need scarce be said, I could never be content with either the one or the other ideal; I want neither that plutocracy grasping and mean, nor that democracy goody and mediocre, occupied solely in turning the other cheek, where would dwell sages without curiosity, who, shunning excess, would not die of disease, but would surely die of ennui. But that is a matter of taste and is not what I wish to discuss.

The question nevertheless remains and should fix our attention; if our choice can only be determined by caprice or by immediate utility, there can be no science for its own sake, and consequently no science. But is that true? That a choice must be made is incontestable; whatever be our activity, facts go quicker than we, and we can not catch them; while the scientist discovers one fact, there happen milliards of milliards in a cubic millimeter of his body. To wish to comprise nature in science would be to want to put the whole into the part.

But scientists believe there is a hierarchy of facts and that among them may be made a judicious choice. They are right, since otherwise there would be no science, yet science exists. One need only open the eyes to see that the conquests of industry which have enriched so many practical men would never have seen the light, if these practical men alone had existed and if they had not been preceded by unselfish devotees who died poor, who never thought of utility, and yet had a guide far other than caprice.

As Mach says, these devotees have spared their successors the trouble of thinking. Those who might have worked solely in view of an immediate application would have left nothing behind them, and, in face of a new need, all must have been begun over again. Now most men do not love to think, and this is perhaps fortunate when instinct guides them, for most often, when they pursue an aim which is immediate and ever the same, instinct guides them better than reason would guide a pure intelligence. But instinct is routine, and if thought did not fecundate it, it would no more progress in man than in the bee or ant. It is needful then to think for those who love not thinking, and, as they are numerous, it is needful that each of our thoughts be as often useful as possible, and this is why a law will be the more precious the more general it is.

This shows us how we should choose: the most interesting facts are those which may serve many times; these are the facts which have a chance of coming up again. We have been so fortunate as to be born in a world where there are such. Suppose that instead of 60 chemical elements there were 60 milliards of them, that they were not some common, the others rare, but that they were uniformly distributed. Then, every time we picked up a new pebble there would be great probability of its being formed of some unknown substance; all that we knew of other pebbles would be worthless for it; before each new object we should be as the new-born babe; like it we could only obey our caprices or our needs. Biologists would be just as much at a loss if there were only individuals and no species and if heredity did not make sons like their fathers.

In such a world there would be no science; perhaps thought and even life would be impossible, since evolution could not there develop the preservational instincts. Happily it is not so; like all good fortune to which we are accustomed, this is not appreciated at its true worth.

Which then are the facts likely to reappear? They are first the simple facts. It is clear that in a complex fact a
thousand circumstances are united by chance, and that only a chance still much less probable could reunite them anew.
But are there any simple facts? And if there are, how recognize them? What assurance is there that a thing we think
simple does not hide a dreadful complexity? All we can say is that we ought to prefer the facts which *seem*
simple to those where our crude eye discerns unlike elements. And then one of two things: either this simplicity is
real, or else the elements are so intimately mingled as not to be distinguishable. In the first case there is chance of
our meeting anew this same simple fact, either in all its purity or entering itself as element in a complex manifold.
In the second case this intimate mixture has likewise more chances of recurring than a heterogeneous assemblage; chance
knows how to mix, it knows not how to disentangle, and to make with multiple elements a well-ordered edifice in which
something is distinguishable, it must be made expressly. The facts which appear simple, even if they are not so, will
therefore be more easily revived by chance. This it is which justifies the method instinctively adopted by the
scientist, and what justifies it still better, perhaps, is that oft-recurring facts appear to us simple, precisely
because we are used to them.

But where is the simple fact? Scientists have been seeking it in the two extremes, in the infinitely great and in the infinitely small. The astronomer has found it because the distances of the stars are immense, so great that each of them appears but as a point, so great that the qualitative differences are effaced, and because a point is simpler than a body which has form and qualities. The physicist on the other hand has sought the elementary phenomenon in fictively cutting up bodies into infinitesimal cubes, because the conditions of the problem, which undergo slow and continuous variation in passing from one point of the body to another, may be regarded as constant in the interior of each of these little cubes. In the same way the biologist has been instinctively led to regard the cell as more interesting than the whole animal, and the outcome has shown his wisdom, since cells belonging to organisms the most different are more alike, for the one who can recognize their resemblances, than are these organisms themselves. The sociologist is more embarrassed; the elements, which for him are men, are too unlike, too variable, too capricious, in a word, too complex; besides, history never begins over again. How then choose the interesting fact, which is that which begins again? Method is precisely the choice of facts; it is needful then to be occupied first with creating a method, and many have been imagined, since none imposes itself, so that sociology is the science which has the most methods and the fewest results.

Therefore it is by the regular facts that it is proper to begin; but after the rule is well established, after it is beyond all doubt, the facts in full conformity with it are erelong without interest since they no longer teach us anything new. It is then the exception which becomes important. We cease to seek resemblances; we devote ourselves above all to the differences, and among the differences are chosen first the most accentuated, not only because they are the most striking, but because they will be the most instructive. A simple example will make my thought plainer: Suppose one wishes to determine a curve by observing some of its points. The practician who concerns himself only with immediate utility would observe only the points he might need for some special object. These points would be badly distributed on the curve; they would be crowded in certain regions, rare in others, so that it would be impossible to join them by a continuous line, and they would be unavailable for other applications. The scientist will proceed differently; as he wishes to study the curve for itself, he will distribute regularly the points to be observed, and when enough are known he will join them by a regular line and then he will have the entire curve. But for that how does he proceed? If he has determined an extreme point of the curve, he does not stay near this extremity, but goes first to the other end; after the two extremities the most instructive point will be the mid-point, and so on.

So when a rule is established we should first seek the cases where this rule has the greatest chance of failing. Thence, among other reasons, come the interest of astronomic facts, and the interest of the geologic past; by going very far away in space or very far away in time, we may find our usual rules entirely overturned, and these grand overturnings aid us the better to see or the better to understand the little changes which may happen nearer to us, in the little corner of the world where we are called to live and act. We shall better know this corner for having traveled in distant countries with which we have nothing to do.

But what we ought to aim at is less the ascertainment of resemblances and differences than the recognition of likenesses hidden under apparent divergences. Particular rules seem at first discordant, but looking more closely we see in general that they resemble each other; different as to matter, they are alike as to form, as to the order of their parts. When we look at them with this bias, we shall see them enlarge and tend to embrace everything. And this it is which makes the value of certain facts which come to complete an assemblage and to show that it is the faithful image of other known assemblages.

I will not further insist, but these few words suffice to show that the scientist does not choose at random the facts he observes. He does not, as Tolstoi says, count the lady-bugs, because, however interesting lady-bugs may be, their number is subject to capricious variations. He seeks to condense much experience and much thought into a slender volume; and that is why a little book on physics contains so many past experiences and a thousand times as many possible experiences whose result is known beforehand.

But we have as yet looked at only one side of the question. The scientist does not study nature because it is useful; he studies it because he delights in it, and he delights in it because it is beautiful. If nature were not beautiful, it would not be worth knowing, and if nature were not worth knowing, life would not be worth living. Of course I do not here speak of that beauty which strikes the senses, the beauty of qualities and of appearances; not that I undervalue such beauty, far from it, but it has nothing to do with science; I mean that profounder beauty which comes from the harmonious order of the parts and which a pure intelligence can grasp. This it is which gives body, a structure so to speak, to the iridescent appearances which flatter our senses, and without this support the beauty of these fugitive dreams would be only imperfect, because it would be vague and always fleeting. On the contrary, intellectual beauty is sufficient unto itself, and it is for its sake, more perhaps than for the future good of humanity, that the scientist devotes himself to long and difficult labors.

It is, therefore, the quest of this especial beauty, the sense of the harmony of the cosmos, which makes us choose the facts most fitting to contribute to this harmony, just as the artist chooses from among the features of his model those which perfect the picture and give it character and life. And we need not fear that this instinctive and unavowed prepossession will turn the scientist aside from the search for the true. One may dream a harmonious world, but how far the real world will leave it behind! The greatest artists that ever lived, the Greeks, made their heavens; how shabby it is beside the true heavens, ours!

And it is because simplicity, because grandeur, is beautiful, that we preferably seek simple facts, sublime facts, that we delight now to follow the majestic course of the stars, now to examine with the microscope that prodigious littleness which is also a grandeur, now to seek in geologic time the traces of a past which attracts because it is far away.

We see too that the longing for the beautiful leads us to the same choice as the longing for the useful. And so it is that this economy of thought, this economy of effort, which is, according to Mach, the constant tendency of science, is at the same time a source of beauty and a practical advantage. The edifices that we admire are those where the architect has known how to proportion the means to the end, where the columns seem to carry gaily, without effort, the weight placed upon them, like the gracious caryatids of the Erechtheum.

Whence comes this concordance? Is it simply that the things which seem to us beautiful are those which best adapt themselves to our intelligence, and that consequently they are at the same time the implement this intelligence knows best how to use? Or is there here a play of evolution and natural selection? Have the peoples whose ideal most conformed to their highest interest exterminated the others and taken their place? All pursued their ideals without reference to consequences, but while this quest led some to destruction, to others it gave empire. One is tempted to believe it. If the Greeks triumphed over the barbarians and if Europe, heir of Greek thought, dominates the world, it is because the savages loved loud colors and the clamorous tones of the drum which occupied only their senses, while the Greeks loved the intellectual beauty which hides beneath sensuous beauty, and this intellectual beauty it is which makes intelligence sure and strong.

Doubtless such a triumph would horrify Tolstoi, and he would not like to acknowledge that it might be truly useful. But this disinterested quest of the true for its own beauty is sane also and able to make man better. I well know that there are mistakes, that the thinker does not always draw thence the serenity he should find therein, and even that there are scientists of bad character. Must we, therefore, abandon science and study only morals? What! Do you think the moralists themselves are irreproachable when they come down from their pedestal?

To foresee the future of mathematics, the true method is to study its history and its present state.

Is this not for us mathematicians in a way a professional procedure? We are accustomed to *extrapolate*,
which is a means of deducing the future from the past and present, and as we well know what this amounts to, we run no
risk of deceiving ourselves about the range of the results it gives us.

We have had hitherto prophets of evil. They blithely reiterate that all problems capable of solution have already been solved, and that nothing is left but gleaning. Happily the case of the past reassures us. Often it was thought all problems were solved or at least an inventory was made of all admitting solution. And then the sense of the word solution enlarged, the insoluble problems became the most interesting of all, and others unforeseen presented themselves. For the Greeks a good solution was one employing only ruler and compasses; then it became one obtained by the extraction of roots, then one using only algebraic or logarithmic functions. The pessimists thus found themselves always outflanked, always forced to retreat, so that at present I think there are no more.

My intention, therefore, is not to combat them, as they are dead; we well know that mathematics will continue to develop, but the question is how, in what direction? You will answer, ‘in every direction,’ and that is partly true; but if it were wholly true it would be a little appalling. Our riches would soon become encumbering and their accumulation would produce a medley as impenetrable as the unknown true was for the ignorant.

The historian, the physicist, even, must make a choice among facts; the head of the scientist, which is only a corner of the universe, could never contain the universe entire; so that among the innumerable facts nature offers, some will be passed by, others retained.

Just so, *a fortiori*, in mathematics; no more can the geometer hold fast pell-mell all the facts presenting
themselves to him; all the more because he it is, almost I had said his caprice, that creates these facts. He
constructs a wholly new combination by putting together its elements; nature does not in general give it to him ready
made.

Doubtless it sometimes happens that the mathematician undertakes a problem to satisfy a need in physics; that the physicist or engineer asks him to calculate a number for a certain application. Shall it be said that we geometers should limit ourselves to awaiting orders, and, in place of cultivating our science for our own delectation, try only to accommodate ourselves to the wants of our patrons? If mathematics has no other object besides aiding those who study nature, it is from these we should await orders. Is this way of looking at it legitimate? Certainly not; if we had not cultivated the exact sciences for themselves, we should not have created mathematics the instrument, and the day the call came from the physicist we should have been helpless.

Nor do the physicists wait to study a phenomenon until some urgent need of material life has made it a necessity for them; and they are right. If the scientists of the eighteenth century had neglected electricity as being in their eyes only a curiosity without practical interest, we should have had in the twentieth century neither telegraphy, nor electro-chemistry, nor electro-technics. The physicists, compelled to choose, are therefore not guided in their choice solely by utility. How then do they choose between the facts of nature? We have explained it in the preceding chapter: the facts which interest them are those capable of leading to the discovery of a law, and so they are analogous to many other facts which do not seem to us isolated, but closely grouped with others. The isolated fact attracts all eyes, those of the layman as well as of the scientist. But what the genuine physicist alone knows how to see, is the bond which unites many facts whose analogy is profound but hidden. The story of Newton’s apple is probably not true, but it is symbolic; let us speak of it then as if it were true. Well then, we must believe that before Newton plenty of men had seen apples fall; not one knew how to conclude anything therefrom. Facts would be sterile were there not minds capable of choosing among them, discerning those behind which something was hidden, and of recognizing what is hiding, minds which under the crude fact perceive the soul of the fact.

We find just the same thing in mathematics. From the varied elements at our disposal we can get millions of different combinations; but one of these combinations, in so far as it is isolated, is absolutely void of value. Often we have taken great pains to construct it, but it serves no purpose, if not perhaps to furnish a task in secondary education. Quite otherwise will it be when this combination shall find place in a class of analogous combinations and we shall have noticed this analogy. We are no longer in the presence of a fact, but of a law. And upon that day the real discoverer will not be the workman who shall have patiently built up certain of these combinations; it will be he who brings to light their kinship. The first will have seen merely the crude fact, only the other will have perceived the soul of the fact. Often to fix this kinship it suffices him to make a new word, and this word is creative. The history of science furnishes us a crowd of examples familiar to all.

The celebrated Vienna philosopher Mach has said that the rôle of science is to produce economy of thought, just as machines produce economy of effort. And that is very true. The savage reckons on his fingers or by heaping pebbles. In teaching children the multiplication table we spare them later innumerable pebble bunchings. Some one has already found out, with pebbles or otherwise, that 6 times 7 is 42 and has had the idea of noting the result, and so we need not do it over again. He did not waste his time even if he reckoned for pleasure: his operation took him only two minutes; it would have taken in all two milliards if a milliard men had had to do it over after him.

The importance of a fact then is measured by its yield, that is to say, by the amount of thought it permits us to spare.

In physics the facts of great yield are those entering into a very general law, since from it they enable us to foresee a great number of others, and just so it is in mathematics. Suppose I have undertaken a complicated calculation and laboriously reached a result: I shall not be compensated for my trouble if thereby I have not become capable of foreseeing the results of other analogous calculations and guiding them with a certainty that avoids the gropings to which one must be resigned in a first attempt. On the other hand, I shall not have wasted my time if these gropings themselves have ended by revealing to me the profound analogy of the problem just treated with a much more extended class of other problems; if they have shown me at once the resemblances and differences of these, if in a word they have made me perceive the possibility of a generalization. Then it is not a new result I have won, it is a new power.

The simple example that comes first to mind is that of an algebraic formula which gives us the solution of a type of numeric problems when finally we replace the letters by numbers. Thanks to it, a single algebraic calculation saves us the pains of ceaselessly beginning over again new numeric calculations. But this is only a crude example; we all know there are analogies inexpressible by a formula and all the more precious.

A new result is of value, if at all, when in unifying elements long known but hitherto separate and seeming strangers one to another it suddenly introduces order where apparently disorder reigned. It then permits us to see at a glance each of these elements and its place in the assemblage. This new fact is not merely precious by itself, but it alone gives value to all the old facts it combines. Our mind is weak as are the senses; it would lose itself in the world’s complexity were this complexity not harmonious; like a near-sighted person, it would see only the details and would be forced to forget each of these details before examining the following, since it would be incapable of embracing all. The only facts worthy our attention are those which introduce order into this complexity and so make it accessible.

Mathematicians attach great importance to the elegance of their methods and their results. This is not pure
dilettantism. What is it indeed that gives us the feeling of elegance in a solution, in a demonstration? It is the
harmony of the diverse parts, their symmetry, their happy balance; in a word it is all that introduces order, all that
gives unity, that permits us to see clearly and to comprehend at once both the *ensemble* and the details. But this is exactly what yields great results; in fact the more we see this aggregate clearly
and at a single glance, the better we perceive its analogies with other neighboring objects, consequently the more
chances we have of divining the possible generalizations. Elegance may produce the feeling of the unforeseen by the
unexpected meeting of objects we are not accustomed to bring together; there again it is fruitful, since it thus
unveils for us kinships before unrecognized. It is fruitful even when it results only from the contrast between the
simplicity of the means and the complexity of the problem set; it makes us then think of the reason for this contrast
and very often makes us see that chance is not the reason; that it is to be found in some unexpected law. In a word,
the feeling of mathematical elegance is only the satisfaction due to any adaptation of the solution to the needs of our
mind, and it is because of this very adaptation that this solution can be for us an instrument. Consequently this
esthetic satisfaction is bound up with the economy of thought. Again the comparison of the Erechtheum comes to my mind,
but I must not use it too often.

It is for the same reason that, when a rather long calculation has led to some simple and striking result, we are
not satisfied until we have shown that we should have been *able to foresee*, if not this entire result, at
least its most characteristic traits. Why? What prevents our being content with a calculation which has told us, it
seems, all we wished to know? It is because, in analogous cases, the long calculation might not again avail, and that
this is not so about the reasoning often half intuitive which would have enabled us to foresee. This reasoning being
short, we see at a single glance all its parts, so that we immediately perceive what must be changed to adapt it to all
the problems of the same nature which can occur. And then it enables us to foresee if the solution of these problems
will be simple, it shows us at least if the calculation is worth undertaking.

What we have just said suffices to show how vain it would be to seek to replace by any mechanical procedure the free initiative of the mathematician. To obtain a result of real value, it is not enough to grind out calculations, or to have a machine to put things in order; it is not order alone, it is unexpected order, which is worth while. The machine may gnaw on the crude fact, the soul of the fact will always escape it.

Since the middle of the last century, mathematicians are more and more desirous of attaining absolute rigor; they are right, and this tendency will be more and more accentuated. In mathematics rigor is not everything, but without it there is nothing. A demonstration which is not rigorous is nothingness. I think no one will contest this truth. But if it were taken too literally, we should be led to conclude that before 1820, for example, there was no mathematics; this would be manifestly excessive; the geometers of that time understood voluntarily what we explain by prolix discourse. This does not mean that they did not see it at all; but they passed over it too rapidly, and to see it well would have necessitated taking the pains to say it.

But is it always needful to say it so many times? Those who were the first to emphasize exactness before all else have given us arguments that we may try to imitate; but if the demonstrations of the future are to be built on this model, mathematical treatises will be very long; and if I fear the lengthenings, it is not solely because I deprecate encumbering libraries, but because I fear that in being lengthened out, our demonstrations may lose that appearance of harmony whose usefulness I have just explained.

The economy of thought is what we should aim at, so it is not enough to supply models for imitation. It is needful for those after us to be able to dispense with these models and, in place of repeating an argument already made, summarize it in a few words. And this has already been attained at times. For instance, there was a type of reasoning found everywhere, and everywhere alike. They were perfectly exact but long. Then all at once the phrase ‘uniformity of convergence’ was hit upon and this phrase made those arguments needless; we were no longer called upon to repeat them, since they could be understood. Those who conquer difficulties then do us a double service: first they teach us to do as they at need, but above all they enable us as often as possible to avoid doing as they, yet without sacrifice of exactness.

We have just seen by one example the importance of words in mathematics, but many others could be cited. It is hard to believe how much a well-chosen word can economize thought, as Mach says. Perhaps I have already said somewhere that mathematics is the art of giving the same name to different things. It is proper that these things, differing in matter, be alike in form, that they may, so to speak, run in the same mold. When the language has been well chosen, we are astonished to see that all the proofs made for a certain object apply immediately to many new objects; there is nothing to change, not even the words, since the names have become the same.

A well-chosen word usually suffices to do away with the exceptions from which the rules stated in the old way suffer; this is why we have created negative quantities, imaginaries, points at infinity, and what not. And exceptions, we must not forget, are pernicious because they hide the laws.

Well, this is one of the characteristics by which we recognize the facts which yield great results. They are those which allow of these happy innovations of language. The crude fact then is often of no great interest; we may point it out many times without having rendered great service to science. It takes value only when a wiser thinker perceives the relation for which it stands, and symbolizes it by a word.

Moreover the physicists do just the same. They have invented the word ‘energy,’ and this word has been prodigiously fruitful, because it also made the law by eliminating the exceptions, since it gave the same name to things differing in matter and like in form.

Among words that have had the most fortunate influence I would select ‘group’ and ‘invariant.’ They have made us see the essence of many mathematical reasonings; they have shown us in how many cases the old mathematicians considered groups without knowing it, and how, believing themselves far from one another, they suddenly found themselves near without knowing why.

To-day we should say that they had dealt with isomorphic groups. We now know that in a group the matter is of little interest, the form alone counts, and that when we know a group we thus know all the isomorphic groups; and thanks to these words ‘group’ and ‘isomorphism,’ which condense in a few syllables this subtile rule and quickly make it familiar to all minds, the transition is immediate and can be done with every economy of thought effort. The idea of group besides attaches to that of transformation. Why do we put such a value on the invention of a new transformation? Because from a single theorem it enables us to get ten or twenty; it has the same value as a zero adjoined to the right of a whole number.

This then it is which has hitherto determined the direction of mathematical advance, and just as certainly will determine it in the future. But to this end the nature of the problems which come up contributes equally. We can not forget what must be our aim. In my opinion this aim is double. Our science borders upon both philosophy and physics, and we work for our two neighbors; so we have always seen and shall still see mathematicians advancing in two opposite directions.

On the one hand, mathematical science must reflect upon itself, and that is useful since reflecting on itself is reflecting on the human mind which has created it, all the more because it is the very one of its creations for which it has borrowed least from without. This is why certain mathematical speculations are useful, such as those devoted to the study of the postulates, of unusual geometries, of peculiar functions. The more these speculations diverge from ordinary conceptions, and consequently from nature and applications, the better they show us what the human mind can create when it frees itself more and more from the tyranny of the external world, the better therefore they let us know it in itself.

But it is toward the other side, the side of nature, that we must direct the bulk of our army. There we meet the physicist or the engineer, who says to us: “Please integrate this differential equation for me; I might need it in a week in view of a construction which should be finished by that time.” “This equation,” we answer, “does not come under one of the integrable types; you know there are not many.” “Yes, I know; but then what good are you?” Usually to understand each other is enough; the engineer in reality does not need the integral in finite terms; he needs to know the general look of the integral function, or he simply wants a certain number which could readily be deduced from this integral if it were known. Usually it is not known, but the number can be calculated without it if we know exactly what number the engineer needs and with what approximation.

Formerly an equation was considered solved only when its solution had been expressed by aid of a finite number of
known functions; but that is possible scarcely once in a hundred times. What we always can do, or rather what we should
always seek to do, is to solve the problem *qualitatively* so to speak; that is to say, seek to know the general
form of the curve which represents the unknown function.

It remains to find the *quantitative* solution of the problem; but if the unknown can not be determined by a
finite calculation, it may always be represented by a convergent infinite series which enables us to calculate it. Can
that be regarded as a true solution? We are told that Newton sent Leibnitz an anagram almost like this: aaaaabbbeeeeij,
etc. Leibnitz naturally understood nothing at all of it; but we, who have the key, know that this anagram meant,
translated into modern terms: “I can integrate all differential equations”; and we are tempted to say that Newton had
either great luck or strange delusions. He merely wished to say he could form (by the method of indeterminate
coefficients) a series of powers formally satisfying the proposed equation.

Such a solution would not satisfy us to-day, and for two reasons: because the convergence is too slow and because the terms follow each other without obeying any law. On the contrary, the series Θ seems to us to leave nothing to be desired, first because it converges very quickly (this is for the practical man who wishes to get at a number as quickly as possible) and next because we see at a glance the law of the terms (this is to satisfy the esthetic need of the theorist).

But then there are no longer solved problems and others which are not; there are only problems *more or less*
solved, according as they are solved by a series converging more or less rapidly, or ruled by a law more or less
harmonious. It often happens however that an imperfect solution guides us toward a better one.
Sometimes the series converges so slowly that the computation is impracticable and we have only succeeded in proving
the possibility of the problem.

And then the engineer finds this a mockery, and justly, since it will not aid him to complete his construction by the date fixed. He little cares to know if it will benefit engineers of the twenty-second century. But as for us, we think differently and we are sometimes happier to have spared our grandchildren a day’s work than to have saved our contemporaries an hour.

Sometimes by groping, empirically, so to speak, we reach a formula sufficiently convergent. “What more do you want?”
says the engineer. And yet, in spite of all, we are not satisfied; we should have liked *to foresee* that
convergence. Why? Because if we had known how to foresee it once, we would know how to foresee it another time. We have
succeeded; that is a small matter in our eyes if we can not validly expect to do so again.

In proportion as science develops, its total comprehension becomes more difficult; then we seek to cut it in pieces and to be satisfied with one of these pieces: in a word, to specialize. If we went on in this way, it would be a grievous obstacle to the progress of science. As we have said, it is by unexpected union between its diverse parts that it progresses. To specialize too much would be to forbid these drawings together. It is to be hoped that congresses like those of Heidelberg and Rome, by putting us in touch with one another, will open for us vistas over neighboring domains and oblige us to compare them with our own, to range somewhat abroad from our own little village; thus they will be the best remedy for the danger just mentioned.

But I have lingered too long over generalities; it is time to enter into detail.

Let us pass in review the various special sciences which combined make mathematics; let us see what each has accomplished, whither it tends and what we may hope from it. If the preceding views are correct, we should see that the greatest advances in the past have happened when two of these sciences have united, when we have become conscious of the similarity of their form, despite the difference of their matter, when they have so modeled themselves upon each other that each could profit by the other’s conquests. We should at the same time foresee in combinations of the same sort the progress of the future.

Progress in arithmetic has been much slower than in algebra and analysis, and it is easy to see why. The feeling of continuity is a precious guide which the arithmetician lacks; each whole number is separated from the others — it has, so to speak, its own individuality. Each of them is a sort of exception and this is why general theorems are rarer in the theory of numbers; this is also why those which exist are more hidden and longer elude the searchers.

If arithmetic is behind algebra and analysis, the best thing for it to do is to seek to model itself upon these sciences so as to profit by their advance. The arithmetician ought therefore to take as guide the analogies with algebra. These analogies are numerous and if, in many cases, they have not yet been studied sufficiently closely to become utilizable, they at least have long been foreseen, and even the language of the two sciences shows they have been recognized. Thus we speak of transcendent numbers and thus we account for the future classification of these numbers already having as model the classification of transcendent functions, and still we do not as yet very well see how to pass from one classification to the other; but had it been seen, it would already have been accomplished and would no longer be the work of the future.

The first example that comes to my mind is the theory of congruences, where is found a perfect parallelism to the theory of algebraic equations. Surely we shall succeed in completing this parallelism, which must hold for instance between the theory of algebraic curves and that of congruences with two variables. And when the problems relative to congruences with several variables shall be solved, this will be a first step toward the solution of many questions of indeterminate analysis.

The theory of algebraic equations will still long hold the attention of geometers; numerous and very different are the sides whence it may be attacked.

We need not think algebra is ended because it gives us rules to form all possible combinations; it remains to find the interesting combinations, those which satisfy such and such a condition. Thus will be formed a sort of indeterminate analysis where the unknowns will no longer be whole numbers, but polynomials. This time it is algebra which will model itself upon arithmetic, following the analogy of the whole number to the integral polynomial with any coefficients or to the integral polynomial with integral coefficients.

It looks as if geometry could contain nothing which is not already included in algebra or analysis; that geometric facts are only algebraic or analytic facts expressed in another language. It might then be thought that after our review there would remain nothing more for us to say relating specially to geometry. This would be to fail to recognize the importance of well-constructed language, not to comprehend what is added to the things themselves by the method of expressing these things and consequently of grouping them.

First the geometric considerations lead us to set ourselves new problems; these may be, if you choose, analytic problems, but such as we never would have set ourselves in connection with analysis. Analysis profits by them however, as it profits by those it has to solve to satisfy the needs of physics.

A great advantage of geometry lies in the fact that in it the senses can come to the aid of thought, and help find the path to follow, and many minds prefer to put the problems of analysis into geometric form. Unhappily our senses can not carry us very far, and they desert us when we wish to soar beyond the classical three dimensions. Does this mean that, beyond the restricted domain wherein they seem to wish to imprison us, we should rely only on pure analysis and that all geometry of more than three dimensions is vain and objectless? The greatest masters of a preceding generation would have answered ‘yes’; to-day we are so familiarized with this notion that we can speak of it, even in a university course, without arousing too much astonishment.

But what good is it? That is easy to see: First it gives us a very convenient terminology, which expresses concisely what the ordinary analytic language would say in prolix phrases. Moreover, this language makes us call like things by the same name and emphasize analogies it will never again let us forget. It enables us therefore still to find our way in this space which is too big for us and which we can not see, always recalling visible space, which is only an imperfect image of it doubtless, but which is nevertheless an image. Here again, as in all the preceding examples, it is analogy with the simple which enables us to comprehend the complex.

This geometry of more than three dimensions is not a simple analytic geometry; it is not purely quantitative, but
qualitative also, and it is in this respect above all that it becomes interesting. There is a science called
*analysis situs* and which has for its object the study of the positional relations of the different elements of
a figure, apart from their sizes. This geometry is purely qualitative; its theorems would remain true if the figures,
instead of being exact, were roughly imitated by a child. We may also make an *analysis situs* of more than
three dimensions. The importance of *analysis situs* is enormous and can not be too much emphasized; the
advantage obtained from it by Riemann, one of its chief creators, would suffice to prove this. We must achieve its
complete construction in the higher spaces; then we shall have an instrument which will enable us really to see in
hyperspace and supplement our senses.

The problems of *analysis situs* would perhaps not have suggested themselves if the analytic language alone
had been spoken; or rather, I am mistaken, they would have occurred surely, since their solution is essential to a
crowd of questions in analysis, but they would have come singly, one after another, and without our being able to
perceive their common bond.

I have spoken above of our need to go back continually to the first principles of our science, and of the advantage
of this for the study of the human mind. This need has inspired two endeavors which have taken a very prominent place
in the most recent annals of mathematics. The first is Cantorism, which has rendered our
science such conspicuous service. Cantor introduced into science a new way of considering mathematical infinity. One of
the characteristic traits of Cantorism is that in place of going up to the general by building up constructions more
and more complicated and defining by construction, it starts from the *genus supremum* and defines only, as the
scholastics would have said, *per genus proximum et differentiam specificam*. Thence comes the horror it has
sometimes inspired in certain minds, for instance in Hermite, whose favorite idea was to compare the mathematical to
the natural sciences. With most of us these prejudices have been dissipated, but it has come to pass that we have
encountered certain paradoxes, certain apparent contradictions that would have delighted Zeno, the Eleatic and the
school of Megara. And then each must seek the remedy. For my part, I think, and I am not the only one, that the
important thing is never to introduce entities not completely definable in a finite number of words. Whatever be the
cure adopted, we may promise ourselves the joy of the doctor called in to follow a beautiful pathologic case.

On the other hand, efforts have been made to enumerate the axioms and postulates, more or less hidden, which serve as foundation to the different theories of mathematics. Professor Hilbert has obtained the most brilliant results. It seems at first that this domain would be very restricted and there would be nothing more to do when the inventory should be ended, which could not take long. But when we shall have enumerated all, there will be many ways of classifying all; a good librarian always finds something to do, and each new classification will be instructive for the philosopher.

Here I end this review which I could not dream of making complete. I think these examples will suffice to show by what mechanism the mathematical sciences have made their progress in the past and in what direction they must advance in the future.

The genesis of mathematical creation is a problem which should intensely interest the psychologist. It is the activity in which the human mind seems to take least from the outside world, in which it acts or seems to act only of itself and on itself, so that in studying the procedure of geometric thought we may hope to reach what is most essential in man’s mind.

This has long been appreciated, and some time back the journal called *L’enseignement mathématique*, edited
by Laisant and Fehr, began an investigation of the mental habits and methods of work of different mathematicians. I had
finished the main outlines of this article when the results of that inquiry were published, so I have hardly been able
to utilize them and shall confine myself to saying that the majority of witnesses confirm my conclusions; I do not say
all, for when the appeal is to universal suffrage unanimity is not to be hoped.

A first fact should surprise us, or rather would surprise us if we were not so used to it. How does it happen there are people who do not understand mathematics? If mathematics invokes only the rules of logic, such as are accepted by all normal minds; if its evidence is based on principles common to all men, and that none could deny without being mad, how does it come about that so many persons are here refractory?

That not every one can invent is nowise mysterious. That not every one can retain a demonstration once learned may also pass. But that not every one can understand mathematical reasoning when explained appears very surprising when we think of it. And yet those who can follow this reasoning only with difficulty are in the majority: that is undeniable, and will surely not be gainsaid by the experience of secondary-school teachers.

And further: how is error possible in mathematics? A sane mind should not be guilty of a logical fallacy, and yet there are very fine minds who do not trip in brief reasoning such as occurs in the ordinary doings of life, and who are incapable of following or repeating without error the mathematical demonstrations which are longer, but which after all are only an accumulation of brief reasonings wholly analogous to those they make so easily. Need we add that mathematicians themselves are not infallible?

The answer seems to me evident. Imagine a long series of syllogisms, and that the conclusions of the first serve as premises of the following: we shall be able to catch each of these syllogisms, and it is not in passing from premises to conclusion that we are in danger of deceiving ourselves. But between the moment in which we first meet a proposition as conclusion of one syllogism, and that in which we reencounter it as premise of another syllogism occasionally some time will elapse, several links of the chain will have unrolled; so it may happen that we have forgotten it, or worse, that we have forgotten its meaning. So it may happen that we replace it by a slightly different proposition, or that, while retaining the same enunciation, we attribute to it a slightly different meaning, and thus it is that we are exposed to error.

Often the mathematician uses a rule. Naturally he begins by demonstrating this rule; and at the time when this proof is fresh in his memory he understands perfectly its meaning and its bearing, and he is in no danger of changing it. But subsequently he trusts his memory and afterward only applies it in a mechanical way; and then if his memory fails him, he may apply it all wrong. Thus it is, to take a simple example, that we sometimes make slips in calculation because we have forgotten our multiplication table.

According to this, the special aptitude for mathematics would be due only to a very sure memory or to a prodigious force of attention. It would be a power like that of the whist-player who remembers the cards played; or, to go up a step, like that of the chess-player who can visualize a great number of combinations and hold them in his memory. Every good mathematician ought to be a good chess-player, and inversely; likewise he should be a good computer. Of course that sometimes happens; thus Gauss was at the same time a geometer of genius and a very precocious and accurate computer.

But there are exceptions; or rather I err; I can not call them exceptions without the exceptions being more than the rule. Gauss it is, on the contrary, who was an exception. As for myself, I must confess, I am absolutely incapable even of adding without mistakes. In the same way I should be but a poor chess-player; I would perceive that by a certain play I should expose myself to a certain danger; I would pass in review several other plays, rejecting them for other reasons, and then finally I should make the move first examined, having meantime forgotten the danger I had foreseen.

In a word, my memory is not bad, but it would be insufficient to make me a good chess-player. Why then does it not
fail me in a difficult piece of mathematical reasoning where most chess-players would lose themselves? Evidently
because it is guided by the general march of the reasoning. A mathematical demonstration is not a simple juxtaposition
of syllogisms, it is syllogisms *placed in a certain order*, and the order in which these elements are placed is
much more important than the elements themselves. If I have the feeling, the intuition, so to speak, of this order, so
as to perceive at a glance the reasoning as a whole, I need no longer fear lest I forget one of the elements, for each
of them will take its allotted place in the array, and that without any effort of memory on my part.

It seems to me then, in repeating a reasoning learned, that I could have invented it. This is often only an illusion; but even then, even if I am not so gifted as to create it by myself, I myself re-invent it in so far as I repeat it.

We know that this feeling, this intuition of mathematical order, that makes us divine hidden harmonies and relations, can not be possessed by every one. Some will not have either this delicate feeling so difficult to define, or a strength of memory and attention beyond the ordinary, and then they will be absolutely incapable of understanding higher mathematics. Such are the majority. Others will have this feeling only in a slight degree, but they will be gifted with an uncommon memory and a great power of attention. They will learn by heart the details one after another; they can understand mathematics and sometimes make applications, but they cannot create. Others, finally, will possess in a less or greater degree the special intuition referred to, and then not only can they understand mathematics even if their memory is nothing extraordinary, but they may become creators and try to invent with more or less success according as this intuition is more or less developed in them.

In fact, what is mathematical creation? It does not consist in making new combinations with mathematical entities already known. Any one could do that, but the combinations so made would be infinite in number and most of them absolutely without interest. To create consists precisely in not making useless combinations and in making those which are useful and which are only a small minority. Invention is discernment, choice.

How to make this choice I have before explained; the mathematical facts worthy of being studied are those which, by their analogy with other facts, are capable of leading us to the knowledge of a mathematical law just as experimental facts lead us to the knowledge of a physical law. They are those which reveal to us unsuspected kinship between other facts, long known, but wrongly believed to be strangers to one another.

Among chosen combinations the most fertile will often be those formed of elements drawn from domains which are far apart. Not that I mean as sufficing for invention the bringing together of objects as disparate as possible; most combinations so formed would be entirely sterile. But certain among them, very rare, are the most fruitful of all.

To invent, I have said, is to choose; but the word is perhaps not wholly exact. It makes one think of a purchaser before whom are displayed a large number of samples, and who examines them, one after the other, to make a choice. Here the samples would be so numerous that a whole lifetime would not suffice to examine them. This is not the actual state of things. The sterile combinations do not even present themselves to the mind of the inventor. Never in the field of his consciousness do combinations appear that are not really useful, except some that he rejects but which have to some extent the characteristics of useful combinations. All goes on as if the inventor were an examiner for the second degree who would only have to question the candidates who had passed a previous examination.

But what I have hitherto said is what may be observed or inferred in reading the writings of the geometers, reading reflectively.

It is time to penetrate deeper and to see what goes on in the very soul of the mathematician. For this, I believe, I can do best by recalling memories of my own. But I shall limit myself to telling how I wrote my first memoir on Fuchsian functions. I beg the reader’s pardon; I am about to use some technical expressions, but they need not frighten him, for he is not obliged to understand them. I shall say, for example, that I have found the demonstration of such a theorem under such circumstances. This theorem will have a barbarous name, unfamiliar to many, but that is unimportant; what is of interest for the psychologist is not the theorem but the circumstances.

For fifteen days I strove to prove that there could not be any functions like those I have since called Fuchsian functions. I was then very ignorant; every day I seated myself at my work table, stayed an hour or two, tried a great number of combinations and reached no results. One evening, contrary to my custom, I drank black coffee and could not sleep. Ideas rose in crowds; I felt them collide until pairs interlocked, so to speak, making a stable combination. By the next morning I had established the existence of a class of Fuchsian functions, those which come from the hypergeometric series; I had only to write out the results, which took but a few hours.

Then I wanted to represent these functions by the quotient of two series; this idea was perfectly conscious and deliberate, the analogy with elliptic functions guided me. I asked myself what properties these series must have if they existed, and I succeeded without difficulty in forming the series I have called theta-Fuchsian.

Just at this time I left Caen, where I was then living, to go on a geologic excursion under the auspices of the school of mines. The changes of travel made me forget my mathematical work. Having reached Coutances, we entered an omnibus to go some place or other. At the moment when I put my foot on the step the idea came to me, without anything in my former thoughts seeming to have paved the way for it, that the transformations I had used to define the Fuchsian functions were identical with those of non-Euclidean geometry. I did not verify the idea; I should not have had time, as, upon taking my seat in the omnibus, I went on with a conversation already commenced, but I felt a perfect certainty. On my return to Caen, for conscience’ sake I verified the result at my leisure.

Then I turned my attention to the study of some arithmetical questions apparently without much success and without a suspicion of any connection with my preceding researches. Disgusted with my failure, I went to spend a few days at the seaside, and thought of something else. One morning, walking on the bluff, the idea came to me, with just the same characteristics of brevity, suddenness and immediate certainty, that the arithmetic transformations of indeterminate ternary quadratic forms were identical with those of non-Euclidean geometry.

Returned to Caen, I meditated on this result and deduced the consequences. The example of quadratic forms showed me that there were Fuchsian groups other than those corresponding to the hypergeometric series; I saw that I could apply to them the theory of theta-Fuchsian series and that consequently there existed Fuchsian functions other than those from the hypergeometric series, the ones I then knew. Naturally I set myself to form all these functions. I made a systematic attack upon them and carried all the outworks, one after another. There was one however that still held out, whose fall would involve that of the whole place. But all my efforts only served at first the better to show me the difficulty, which indeed was something. All this work was perfectly conscious.

Thereupon I left for Mont-Valérien, where I was to go through my military service; so I was very differently occupied. One day, going along the street, the solution of the difficulty which had stopped me suddenly appeared to me. I did not try to go deep into it immediately, and only after my service did I again take up the question. I had all the elements and had only to arrange them and put them together. So I wrote out my final memoir at a single stroke and without difficulty.

I shall limit myself to this single example; it is useless to multiply them. In regard to my other researches I
would have to say analogous things, and the observations of other mathematicians given in *L’enseignement
mathématique* would only confirm them.

Most striking at first is this appearance of sudden illumination, a manifest sign of long, unconscious prior work. The rôle of this unconscious work in mathematical invention appears to me incontestable, and traces of it would be found in other cases where it is less evident. Often when one works at a hard question, nothing good is accomplished at the first attack. Then one takes a rest, longer or shorter, and sits down anew to the work. During the first half-hour, as before, nothing is found, and then all of a sudden the decisive idea presents itself to the mind. It might be said that the conscious work has been more fruitful because it has been interrupted and the rest has given back to the mind its force and freshness. But it is more probable that this rest has been filled out with unconscious work and that the result of this work has afterward revealed itself to the geometer just as in the cases I have cited; only the revelation, instead of coming during a walk or a journey, has happened during a period of conscious work, but independently of this work which plays at most a rôle of excitant, as if it were the goad stimulating the results already reached during rest, but remaining unconscious, to assume the conscious form.

There is another remark to be made about the conditions of this unconscious work: it is possible, and of a certainty it is only fruitful, if it is on the one hand preceded and on the other hand followed by a period of conscious work. These sudden inspirations (and the examples already cited sufficiently prove this) never happen except after some days of voluntary effort which has appeared absolutely fruitless and whence nothing good seems to have come, where the way taken seems totally astray. These efforts then have not been as sterile as one thinks; they have set agoing the unconscious machine and without them it would not have moved and would have produced nothing.

The need for the second period of conscious work, after the inspiration, is still easier to understand. It is necessary to put in shape the results of this inspiration, to deduce from them the immediate consequences, to arrange them, to word the demonstrations, but above all is verification necessary. I have spoken of the feeling of absolute certitude accompanying the inspiration; in the cases cited this feeling was no deceiver, nor is it usually. But do not think this a rule without exception; often this feeling deceives us without being any the less vivid, and we only find it out when we seek to put on foot the demonstration. I have especially noticed this fact in regard to ideas coming to me in the morning or evening in bed while in a semi-hypnagogic state.

Such are the realities; now for the thoughts they force upon us. The unconscious, or, as we say, the subliminal self plays an important rôle in mathematical creation; this follows from what we have said. But usually the subliminal self is considered as purely automatic. Now we have seen that mathematical work is not simply mechanical, that it could not be done by a machine, however perfect. It is not merely a question of applying rules, of making the most combinations possible according to certain fixed laws. The combinations so obtained would be exceedingly numerous, useless and cumbersome. The true work of the inventor consists in choosing among these combinations so as to eliminate the useless ones or rather to avoid the trouble of making them, and the rules which must guide this choice are extremely fine and delicate. It is almost impossible to state them precisely; they are felt rather than formulated. Under these conditions, how imagine a sieve capable of applying them mechanically?

A first hypothesis now presents itself: the subliminal self is in no way inferior to the conscious self; it is not
purely automatic; it is capable of discernment; it has tact, delicacy; it knows how to choose, to divine. What do I
say? It knows better how to divine than the conscious self, since it succeeds where that has failed. In a word, is not
the subliminal self superior to the conscious self? You recognize the full importance of this question. Boutroux in a
recent lecture has shown how it came up on a very different occasion, and what consequences would follow an affirmative
answer. (See also, by the same author, *Science et Religion*, pp. 313 ff.)

Is this affirmative answer forced upon us by the facts I have just given? I confess that, for my part, I should hate to accept it. Reexamine the facts then and see if they are not compatible with another explanation.

It is certain that the combinations which present themselves to the mind in a sort of sudden illumination, after an unconscious working somewhat prolonged, are generally useful and fertile combinations, which seem the result of a first impression. Does it follow that the subliminal self, having divined by a delicate intuition that these combinations would be useful, has formed only these, or has it rather formed many others which were lacking in interest and have remained unconscious?

In this second way of looking at it, all the combinations would be formed in consequence of the automatism of the subliminal self, but only the interesting ones would break into the domain of consciousness. And this is still very mysterious. What is the cause that, among the thousand products of our unconscious activity, some are called to pass the threshold, while others remain below? Is it a simple chance which confers this privilege? Evidently not; among all the stimuli of our senses, for example, only the most intense fix our attention, unless it has been drawn to them by other causes. More generally the privileged unconscious phenomena, those susceptible of becoming conscious, are those which, directly or indirectly, affect most profoundly our emotional sensibility.

It may be surprising to see emotional sensibility invoked *à propos* of mathematical demonstrations which, it
would seem, can interest only the intellect. This would be to forget the feeling of mathematical beauty, of the harmony
of numbers and forms, of geometric elegance. This is a true esthetic feeling that all real mathematicians know, and
surely it belongs to emotional sensibility.

Now, what are the mathematic entities to which we attribute this character of beauty and elegance, and which are capable of developing in us a sort of esthetic emotion? They are those whose elements are harmoniously disposed so that the mind without effort can embrace their totality while realizing the details. This harmony is at once a satisfaction of our esthetic needs and an aid to the mind, sustaining and guiding; And at the same time, in putting under our eyes a well-ordered whole, it makes us foresee a mathematical law. Now, as we have said above, the only mathematical facts worthy of fixing our attention and capable of being useful are those which can teach us a mathematical law. So that we reach the following conclusion: The useful combinations are precisely the most beautiful, I mean those best able to charm this special sensibility that all mathematicians know, but of which the profane are so ignorant as often to be tempted to smile at it.

What happens then? Among the great numbers of combinations blindly formed by the subliminal self, almost all are without interest and without utility; but just for that reason they are also without effect upon the esthetic sensibility. Consciousness will never know them; only certain ones are harmonious, and, consequently, at once useful and beautiful. They will be capable of touching this special sensibility of the geometer of which I have just spoken, and which, once aroused, will call our attention to them, and thus give them occasion to become conscious.

This is only a hypothesis, and yet here is an observation which may confirm it: when a sudden illumination seizes upon the mind of the mathematician, it usually happens that it does not deceive him, but it also sometimes happens, as I have said, that it does not stand the test of verification; well, we almost always notice that this false idea, had it been true, would have gratified our natural feeling for mathematical elegance.

Thus it is this special esthetic sensibility which plays the rôle of the delicate sieve of which I spoke, and that sufficiently explains why the one lacking it will never be a real creator.

Yet all the difficulties have not disappeared. The conscious self is narrowly limited, and as for the subliminal
self we know not its limitations, and this is why we are not too reluctant in supposing that it has been able in a
short time to make more different combinations than the whole life of a conscious being could encompass. Yet these
limitations exist. Is it likely that it is able to form all the possible combinations, whose number would frighten the
imagination? Nevertheless that would seem necessary, because if it produces only a small part of these combinations,
and if it makes them at random, there would be small chance that the *good*, the one we
should choose, would be found among them.

Perhaps we ought to seek the explanation in that preliminary period of conscious work which always precedes all fruitful unconscious labor. Permit me a rough comparison. Figure the future elements of our combinations as something like the hooked atoms of Epicurus. During the complete repose of the mind, these atoms are motionless, they are, so to speak, hooked to the wall; so this complete rest may be indefinitely prolonged without the atoms meeting, and consequently without any combination between them.

On the other hand, during a period of apparent rest and unconscious work, certain of them are detached from the wall and put in motion. They flash in every direction through the space (I was about to say the room) where they are enclosed, as would, for example, a swarm of gnats or, if you prefer a more learned comparison, like the molecules of gas in the kinematic theory of gases. Then their mutual impacts may produce new combinations.

What is the rôle of the preliminary conscious work? It is evidently to mobilize certain of these atoms, to unhook them from the wall and put them in swing. We think we have done no good, because we have moved these elements a thousand different ways in seeking to assemble them, and have found no satisfactory aggregate. But, after this shaking up imposed upon them by our will, these atoms do not return to their primitive rest. They freely continue their dance.

Now, our will did not choose them at random; it pursued a perfectly determined aim. The mobilized atoms are therefore not any atoms whatsoever; they are those from which we might reasonably expect the desired solution. Then the mobilized atoms undergo impacts which make them enter into combinations among themselves or with other atoms at rest which they struck against in their course. Again I beg pardon, my comparison is very rough, but I scarcely know how otherwise to make my thought understood.

However it may be, the only combinations that have a chance of forming are those where at least one of the elements
is one of those atoms freely chosen by our will. Now, it is evidently among these that is found
what I called the *good combination*. Perhaps this is a way of lessening the paradoxical in the original
hypothesis.

Another observation. It never happens that the unconscious work gives us the result of a somewhat long calculation
*all made*, where we have only to apply fixed rules. We might think the wholly automatic subliminal self
particularly apt for this sort of work, which is in a way exclusively mechanical. It seems that thinking in the evening
upon the factors of a multiplication we might hope to find the product ready made upon our awakening, or again that an
algebraic calculation, for example a verification, would be made unconsciously. Nothing of the sort, as observation
proves. All one may hope from these inspirations, fruits of unconscious work, is a point of departure for such
calculations. As for the calculations themselves, they must be made in the second period of conscious work, that which
follows the inspiration, that in which one verifies the results of this inspiration and deduces their consequences. The
rules of these calculations are strict and complicated. They require discipline, attention, will, and therefore
consciousness. In the subliminal self, on the contrary, reigns what I should call liberty, if we might give this name
to the simple absence of discipline and to the disorder born of chance. Only, this disorder itself permits unexpected
combinations.

I shall make a last remark: when above I made certain personal observations, I spoke of a night of excitement when I worked in spite of myself. Such cases are frequent, and it is not necessary that the abnormal cerebral activity be caused by a physical excitant as in that I mentioned. It seems, in such cases, that one is present at his own unconscious work, made partially perceptible to the over-excited consciousness, yet without having changed its nature. Then we vaguely comprehend what distinguishes the two mechanisms or, if you wish, the working methods of the two egos. And the psychologic observations I have been able thus to make seem to me to confirm in their general outlines the views I have given.

Surely they have need of it, for they are and remain in spite of all very hypothetical: the interest of the questions is so great that I do not repent of having submitted them to the reader.

“How dare we speak of the laws of chance? Is not chance the antithesis of all law?” So says Bertrand at the
beginning of his *Calcul des probabiltités*. Probability is opposed to certitude; so it is what we do not know
and consequently it seems what we could not calculate. Here is at least apparently a contradiction, and about it much
has already been written.

And first, what is chance? The ancients distinguished between phenomena seemingly obeying harmonious laws, established once for all, and those which they attributed to chance; these were the ones unpredictable because rebellious to all law. In each domain the precise laws did not decide everything, they only drew limits between which chance might act. In this conception the word chance had a precise and objective meaning; what was chance for one was also chance for another and even for the gods.

But this conception is not ours to-day. We have become absolute determinists, and even those who want to reserve the rights of human free will let determinism reign undividedly in the inorganic world at least. Every phenomenon, however minute, has a cause; and a mind infinitely powerful, infinitely well-informed about the laws of nature, could have foreseen it from the beginning of the centuries. If such a mind existed, we could not play with it at any game of chance; we should always lose.

In fact for it the word chance would not have any meaning, or rather there would be no chance. It is because of our weakness and our ignorance that the word has a meaning for us. And, even without going beyond our feeble humanity, what is chance for the ignorant is not chance for the scientist. Chance is only the measure of our ignorance. Fortuitous phenomena are, by definition, those whose laws we do not know.

But is this definition altogether satisfactory? When the first Chaldean shepherds followed
with their eyes the movements of the stars, they knew not as yet the laws of astronomy; would they have dreamed of
saying that the stars move at random? If a modern physicist studies a new phenomenon, and if he discovers its law
Tuesday, would he have said Monday that this phenomenon was fortuitous? Moreover, do we not often invoke what Bertrand
calls the laws of chance, to predict a phenomenon? For example, in the kinetic theory of gases we obtain the known laws
of Mariotte and of Gay-Lussac by means of the hypothesis that the velocities of the molecules of gas vary irregularly,
that is to say at random. All physicists will agree that the observable laws would be much less simple if the
velocities were ruled by any simple elementary law whatsoever, if the molecules were, as we say, *organized*, if
they were subject to some discipline. It is due to chance, that is to say, to our ignorance, that we can draw our
conclusions; and then if the word chance is simply synonymous with ignorance what does that mean? Must we therefore
translate as follows?

“You ask me to predict for you the phenomena about to happen. If, unluckily, I knew the laws of these phenomena I could make the prediction only by inextricable calculations and would have to renounce attempting to answer you; but as I have the good fortune not to know them, I will answer you at once. And what is most surprising, my answer will be right.”

So it must well be that chance is something other than the name we give our ignorance, that among phenomena whose causes are unknown to us we must distinguish fortuitous phenomena about which the calculus of probabilities will provisionally give information, from those which are not fortuitous and of which we can say nothing so long as we shall not have determined the laws governing them. For the fortuitous phenomena themselves, it is clear that the information given us by the calculus of probabilities will not cease to be true upon the day when these phenomena shall be better known.

The director of a life insurance company does not know when each of the insured will die, but he relies upon the calculus of probabilities and on the law of great numbers, and he is not deceived, since he distributes dividends to his stockholders. These dividends would not vanish if a very penetrating and very indiscreet physician should, after the policies were signed, reveal to the director the life chances of the insured. This doctor would dissipate the ignorance of the director, but he would have no influence on the dividends, which evidently are not an outcome of this ignorance.

To find a better definition of chance we must examine some of the facts which we agree to regard as fortuitous, and to which the calculus of probabilities seems to apply; we then shall investigate what are their common characteristics.

The first example we select is that of unstable equilibrium; if a cone rests upon its apex, we know well that it will fall, but we do not know toward what side; it seems to us chance alone will decide. If the cone were perfectly symmetric, if its axis were perfectly vertical, if it were acted upon by no force other than gravity, it would not fall at all. But the least defect in symmetry will make it lean slightly toward one side or the other, and if it leans, however little, it will fall altogether toward that side. Even if the symmetry were perfect, a very slight tremor, a breath of air could make it incline some seconds of arc; this will be enough to determine its fall and even the sense of its fall which will be that of the initial inclination.

A very slight cause, which escapes us, determines a considerable effect which we can not help seeing, and then we
say this effect is due to chance. If we could know exactly the laws of nature and the situation of the universe at the
initial instant, we should be able to predict exactly the situation of this same universe at a subsequent instant. But
even when the natural laws should have no further secret for us, we could know the initial situation only
*approximately*. If that permits us to foresee the subsequent situation *with the same degree of
approximation*, this is all we require, we say the phenomenon has been predicted, that it is ruled by laws. But
this is not always the case; it may happen that slight differences in the initial conditions produce very great
differences in the final phenomena; a slight error in the former would make an enormous error in the latter. Prediction becomes impossible and we have the fortuitous phenomenon.

Our second example will be very analogous to the first and we shall take it from meteorology. Why have the meteorologists such difficulty in predicting the weather with any certainty? Why do the rains, the tempests themselves seem to us to come by chance, so that many persons find it quite natural to pray for rain or shine, when they would think it ridiculous to pray for an eclipse? We see that great perturbations generally happen in regions where the atmosphere is in unstable equilibrium. The meteorologists are aware that this equilibrium is unstable, that a cyclone is arising somewhere; but where they can not tell; one-tenth of a degree more or less at any point, and the cyclone bursts here and not there, and spreads its ravages over countries it would have spared. This we could have foreseen if we had known that tenth of a degree, but the observations were neither sufficiently close nor sufficiently precise, and for this reason all seems due to the agency of chance. Here again we find the same contrast between a very slight cause, unappreciable to the observer, and important effects, which are sometimes tremendous disasters.

Let us pass to another example, the distribution of the minor planets on the zodiac. Their initial longitudes may
have been any longitudes whatever; but their mean motions were different and they have revolved for so long a time that
we may say they are now distributed *at random* along the zodiac. Very slight initial differences between their
distances from the sun, or, what comes to the same thing, between their mean motions, have ended by giving enormous
differences between their present longitudes. An excess of the thousandth of a second in the daily mean motion will
give in fact a second in three years, a degree in ten thousand years, an entire circumference in three or four million
years, and what is that to the time which has passed since the minor planets detached themselves from the nebula of
Laplace? Again therefore we see a slight cause and a great effect; or better, slight differences in the cause and great
differences in the effect.

The game of roulette does not take us as far as might seem from the preceding example. Assume a needle to be turned on a pivot over a dial divided into a hundred sectors alternately red and black. If it stops on a red sector I win; if not, I lose. Evidently all depends upon the initial impulse I give the needle. The needle will make, suppose, ten or twenty turns, but it will stop sooner or not so soon, according as I shall have pushed it more or less strongly. It suffices that the impulse vary only by a thousandth or a two thousandth to make the needle stop over a black sector or over the following red one. These are differences the muscular sense can not distinguish and which elude even the most delicate instruments. So it is impossible for me to foresee what the needle I have started will do, and this is why my heart throbs and I hope everything from luck. The difference in the cause is imperceptible, and the difference in the effect is for me of the highest importance, since it means my whole stake.

Permit me, in this connection, a thought somewhat foreign to my subject. Some years ago a philosopher said that the future is determined by the past, but not the past by the future; or, in other words, from knowledge of the present we could deduce the future, but not the past; because, said he, a cause can have only one effect, while the same effect might be produced by several different causes. It is clear no scientist can subscribe to this conclusion. The laws of nature bind the antecedent to the consequent in such a way that the antecedent is as well determined by the consequent as the consequent by the antecedent. But whence came the error of this philosopher? We know that in virtue of Carnot’s principle physical phenomena are irreversible and the world tends toward uniformity. When two bodies of different temperature come in contact, the warmer gives up heat to the colder; so we may foresee that the temperature will equalize. But once equal, if asked about the anterior state, what can we answer? We might say that one was warm and the other cold, but not be able to divine which formerly was the warmer.

And yet in reality the temperatures will never reach perfect equality. The difference of the temperatures only tends asymptotically toward zero. There comes a moment when our thermometers are powerless to make it known. But if we had thermometers a thousand times, a hundred thousand times as sensitive, we should recognize that there still is a slight difference, and that one of the bodies remains a little warmer than the other, and so we could say this it is which formerly was much the warmer.

So then there are, contrary to what we found in the former examples, great differences in cause and slight differences in effect. Flammarion once imagined an observer going away from the earth with a velocity greater than that of light; for him time would have changed sign. History would be turned about, and Waterloo would precede Austerlitz. Well, for this observer, effects and causes would be inverted; unstable equilibrium would no longer be the exception. Because of the universal irreversibility, all would seem to him to come out of a sort of chaos in unstable equilibrium. All nature would appear to him delivered over to chance.

Now for other examples where we shall see somewhat different characteristics. Take first the kinetic theory of gases. How should we picture a receptacle filled with gas? Innumerable molecules, moving at high speeds, flash through this receptacle in every direction. At every instant they strike against its walls or each other, and these collisions happen under the most diverse conditions. What above all impresses us here is not the littleness of the causes, but their complexity, and yet the former element is still found here and plays an important rôle. If a molecule deviated right or left from its trajectory, by a very small quantity, comparable to the radius of action of the gaseous molecules, it would avoid a collision or sustain it under different conditions, and that would vary the direction of its velocity after the impact, perhaps by ninety degrees or by a hundred and eighty degrees.

And this is not all; we have just seen that it is necessary to deflect the molecule before the clash by only an
infinitesimal, to produce its deviation after the collision by a finite quantity. If then the molecule undergoes two
successive shocks, it will suffice to deflect it before the first by an infinitesimal of the second order, for it to
deviate after the first encounter by an infinitesimal of the first order, and after the second
hit, by a finite quantity. And the molecule will not undergo merely two shocks; it will undergo a very great number per
second. So that if the first shock has multiplied the deviation by a very large number *A*, after *n*
shocks it will be multiplied by *A ^{n}*. It will therefore become very great not merely because

Take a second example. Why do the drops of rain in a shower seem to be distributed at random? This is again because of the complexity of the causes which determine their formation. Ions are distributed in the atmosphere. For a long while they have been subjected to air-currents constantly changing, they have been caught in very small whirlwinds, so that their final distribution has no longer any relation to their initial distribution. Suddenly the temperature falls, vapor condenses, and each of these ions becomes the center of a drop of rain. To know what will be the distribution of these drops and how many will fall on each paving-stone, it would not be sufficient to know the initial situation of the ions, it would be necessary to compute the effect of a thousand little capricious air-currents.

And again it is the same if we put grains of powder in suspension in water. The vase is ploughed by currents whose law we know not, we only know it is very complicated. At the end of a certain time the grains will be distributed at random, that is to say uniformly, in the vase; and this is due precisely to the complexity of these currents. If they obeyed some simple law, if for example the vase revolved and the currents circulated around the axis of the vase, describing circles, it would no longer be the same, since each grain would retain its initial altitude and its initial distance from the axis.

We should reach the same result in considering the mixing of two liquids or of two fine-grained powders. And to take
a grosser example, this is also what happens when we shuffle playing-cards. At each stroke the cards undergo a
permutation (analogous to that studied in the theory of substitutions). What will happen? The probability of a
particular permutation (for example, that bringing to the *n*th place the card occupying
the ϕ(*n*)th place before the permutation) depends upon the player’s habits. But if this player shuffles the
cards long enough, there will be a great number of successive permutations, and the resulting final order will no
longer be governed by aught but chance; I mean to say that all possible orders will be equally probable. It is to the
great number of successive permutations, that is to say to the complexity of the phenomenon, that this result is
due.

A final word about the theory of errors. Here it is that the causes are complex and multiple. To how many snares is not the observer exposed, even with the best instrument! He should apply himself to finding out the largest and avoiding them. These are the ones giving birth to systematic errors. But when he has eliminated those, admitting that he succeeds, there remain many small ones which, their effects accumulating, may become dangerous. Thence come the accidental errors; and we attribute them to chance because their causes are too complicated and too numerous. Here again we have only little causes, but each of them would produce only a slight effect; it is by their union and their number that their effects become formidable.

We may take still a third point of view, less important than the first two and upon which I shall lay less stress. When we seek to foresee an event and examine its antecedents, we strive to search into the anterior situation. This could not be done for all parts of the universe and we are content to know what is passing in the neighborhood of the point where the event should occur, or what would appear to have some relation to it. An examination can not be complete and we must know how to choose. But it may happen that we have passed by circumstances which at first sight seemed completely foreign to the foreseen happening, to which one would never have dreamed of attributing any influence and which nevertheless, contrary to all anticipation, come to play an important rôle.

A man passes in the street going to his business; some one knowing the business could have told why he started at such a time and went by such a street. On the roof works a tiler. The contractor employing him could in a certain measure foresee what he would do. But the passer-by scarcely thinks of the tiler, nor the tiler of him; they seem to belong to two worlds completely foreign to one another. And yet the tiler drops a tile which kills the man, and we do not hesitate to say this is chance.

Our weakness forbids our considering the entire universe and makes us cut it up into slices. We try to do this as little artificially as possible. And yet it happens from time to time that two of these slices react upon each other. The effects of this mutual action then seem to us to be due to chance.

Is this a third way of conceiving chance? Not always; in fact most often we are carried back to the first or the second. Whenever two worlds usually foreign to one another come thus to react upon each other, the laws of this reaction must be very complex. On the other hand, a very slight change in the initial conditions of these two worlds would have been sufficient for the reaction not to have happened. How little was needed for the man to pass a second later or the tiler to drop his tile a second sooner.

All we have said still does not explain why chance obeys laws. Does the fact that the causes are slight or complex
suffice for our foreseeing, if not their effects *in each case*, at least what their effects will be, *on the
average*? To answer this question we had better take up again some of the examples already cited.

I shall begin with that of the roulette. I have said that the point where the needle will stop depends upon the
initial push given it. What is the probability of this push having this or that value? I know nothing about it, but it
is difficult for me not to suppose that this probability is represented by a continuous analytic function. The
probability that the push is comprised between α and α + ε will then be sensibly equal to the probability of its being
comprised between α + ε and α + 2ε, *provided* ε *be very small*. This is a property common to all
analytic functions. Minute variations of the function are proportional to minute variations of the variable.

But we have assumed that an exceedingly slight variation of the push suffices to change the color of the sector over which the needle finally stops. From α to α + ε it is red, from α + ε to α + 2ε it is black; the probability of each red sector is therefore the same as of the following black, and consequently the total probability of red equals the total probability of black.

The datum of the question is the analytic function representing the probability of a particular initial push. But the theorem remains true whatever be this datum, since it depends upon a property common to all analytic functions. From this it follows finally that we no longer need the datum.

What we have just said for the case of the roulette applies also to the example of the minor planets. The zodiac may be regarded as an immense roulette on which have been tossed many little balls with different initial impulses varying according to some law. Their present distribution is uniform and independent of this law, for the same reason as in the preceding case. Thus we see why phenomena obey the laws of chance when slight differences in the causes suffice to bring on great differences in the effects. The probabilities of these slight differences may then be regarded as proportional to these differences themselves, just because these differences are minute, and the infinitesimal increments of a continuous function are proportional to those of the variable.

Take an entirely different example, where intervenes especially the complexity of the causes. Suppose a player shuffles a pack of cards. At each shuffle he changes the order of the cards, and he may change them in many ways. To simplify the exposition, consider only three cards. The cards which before the shuffle occupied respectively the places 123, may after the shuffle occupy the places

123, 231, 312, 321, 132, 213.

Each of these six hypotheses is possible and they have respectively for probabilities:

*p*_{1}, *p*_{2}, *p*_{3}, *p*_{4},
*p*_{5}, *p*_{6}.

The sum of these six numbers equals 1; but this is all we know of them; these six probabilities depend naturally upon the habits of the player which we do not know.

At the second shuffle and the following, this will recommence, and under the same conditions; I mean that
*p*_{4} for example represents always the probability that the three cards which occupied after the
*n*th shuffle and before the *n* + 1th the places 123, occupy the places 321 after the *n* + 1th
shuffle. And this remains true whatever be the number *n*, since the habits of the player and his way of
shuffling remain the same.

But if the number of shuffles is very great, the cards which before the first shuffle occupied the places 123 may, after the last shuffle, occupy the places

123, 231, 312, 321, 132, 213

and the probability of these six hypotheses will be sensibly the same and equal to 1/6; and this will
be true whatever be the numbers *p*_{1} . . . *p*_{6} which we do not know. The
great number of shuffles, that is to say the complexity of the causes, has produced uniformity.

This would apply without change if there were more than three cards, but even with three cards the demonstration
would be complicated; let it suffice to give it for only two cards. Then we have only two possibilities 12, 21 with the
probabilities *p*_{1} and *p*_{2} = 1 − *p*_{1}.

Suppose *n* shuffles and suppose I win one franc if the cards are finally in the initial order and lose one
if they are finally inverted. Then, my mathematical expectation will be (*p*_{1} −
*p*_{2})^{n}.

The difference *p*_{1} − *p*_{2} is certainly less than 1; so that if *n* is
very great my expectation will be zero; we need not learn *p*_{1} and *p*_{2} to be aware
that the game is equitable.

There would always be an exception if one of the numbers *p*_{1} and *p*_{2} was equal
to 1 and the other naught. *Then it would not apply because our initial hypotheses would be too simple.*

What we have just seen applies not only to the mixing of cards, but to all mixings, to those of powders and of liquids; and even to those of the molecules of gases in the kinetic theory of gases.

To return to this theory, suppose for a moment a gas whose molecules can not mutually clash, but may be deviated by hitting the insides of the vase wherein the gas is confined. If the form of the vase is sufficiently complex the distribution of the molecules and that of the velocities will not be long in becoming uniform. But this will not be so if the vase is spherical or if it has the shape of a cuboid. Why? Because in the first case the distance from the center to any trajectory will remain constant; in the second case this will be the absolute value of the angle of each trajectory with the faces of the cuboid.

So we see what should be understood by conditions *too simple*; they are those which conserve something,
which leave an invariant remaining. Are the differential equations of the problem too simple for us to apply the laws
of chance? This question would seem at first view to lack precise meaning; now we know what it means. They are too
simple if they conserve something, if they admit a uniform integral. If something in the initial conditions remains
unchanged, it is clear the final situation can no longer be independent of the initial situation.

We come finally to the theory of errors. We know not to what are due the accidental errors, and precisely because we do not know, we are aware they obey the law of Gauss. Such is the paradox. The explanation is nearly the same as in the preceding cases. We need know only one thing: that the errors are very numerous, that they are very slight, that each may be as well negative as positive. What is the curve of probability of each of them? We do not know; we only suppose it is symmetric. We prove then that the resultant error will follow Gauss’s law, and this resulting law is independent of the particular laws which we do not know. Here again the simplicity of the result is born of the very complexity of the data.

But we are not through with paradoxes. I have just recalled the figment of Flammarion, that of the man going quicker than light, for whom time changes sign. I said that for him all phenomena would seem due to chance. That is true from a certain point of view, and yet all these phenomena at a given moment would not be distributed in conformity with the laws of chance, since the distribution would be the same as for us, who, seeing them unfold harmoniously and without coming out of a primal chaos, do not regard them as ruled by chance.

What does that mean? For Lumen, Flammarion’s man, slight causes seem to produce great effects; why do not things go on as for us when we think we see grand effects due to little causes? Would not the same reasoning be applicable in his case?

Let us return to the argument. When slight differences in the causes produce vast differences in the effects, why are these effects distributed according to the laws of chance? Suppose a difference of a millimeter in the cause produces a difference of a kilometer in the effect. If I win in case the effect corresponds to a kilometer bearing an even number, my probability of winning will be 1/2. Why? Because to make that, the cause must correspond to a millimeter with an even number. Now, according to all appearance, the probability of the cause varying between certain limits will be proportional to the distance apart of these limits, provided this distance be very small. If this hypothesis were not admitted there would no longer be any way of representing the probability by a continuous function.

What now will happen when great causes produce small effects? This is the case where we should not attribute the
phenomenon to chance and where on the contrary Lumen would attribute it to chance. To a difference of a kilometer in
the cause would correspond a difference of a millimeter in the effect. Would the probability of the cause being
comprised between two limits *n* kilometers apart still be proportional to *n*? We have no reason to
suppose so, since this distance, *n* kilometers, is great. But the probability that the effect lies between two
limits *n* millimeters apart will be precisely the same, so it will not be proportional to *n*, even
though this distance, *n* millimeters, be small. There is no way therefore of representing the law of
probability of effects by a continuous curve. This curve, understand, may remain continuous in the *analytic*
sense of the word; to *infinitesimal* variations of the abscissa will correspond infinitesimal variations of the
ordinate. But *practically* it will not be continuous, since *very small* variations of the ordinate
would not correspond to very small variations of the abscissa. It would become impossible to trace the curve with an
ordinary pencil; that is what I mean.

So what must we conclude? Lumen has no right to say that the probability of the cause
(*his* cause, our effect) should be represented necessarily by a continuous function. But then why have we this
right? It is because this state of unstable equilibrium which we have been calling initial is itself only the final
outcome of a long previous history. In the course of this history complex causes have worked a great while: they have
contributed to produce the mixture of elements and they have tended to make everything uniform at least within a small
region; they have rounded off the corners, smoothed down the hills and filled up the valleys. However capricious and
irregular may have been the primitive curve given over to them, they have worked so much toward making it regular that
finally they deliver over to us a continuous curve. And this is why we may in all confidence assume its continuity.

Lumen would not have the same reasons for such a conclusion. For him complex causes would not seem agents of equalization and regularity, but on the contrary would create only inequality and differentiation. He would see a world more and more varied come forth from a sort of primitive chaos. The changes he could observe would be for him unforeseen and impossible to foresee. They would seem to him due to some caprice or another; but this caprice would be quite different from our chance, since it would be opposed to all law, while our chance still has its laws. All these points call for lengthy explications, which perhaps would aid in the better comprehension of the irreversibility of the universe.

We have sought to define chance, and now it is proper to put a question. Has chance thus defined, in so far as this is possible, objectivity?

It may be questioned. I have spoken of very slight or very complex causes. But what is very little for one may be very big for another, and what seems very complex to one may seem simple to another. In part I have already answered by saying precisely in what cases differential equations become too simple for the laws of chance to remain applicable. But it is fitting to examine the matter a little more closely, because we may take still other points of view.

What means the phrase ‘very slight’? To understand it we need only go back to what has already been said. A
difference is very slight, an interval is very small, when within the limits of this interval the probability remains
sensibly constant. And why may this probability be regarded as constant within a small interval? It is because we
assume that the law of probability is represented by a continuous curve, continuous not only in the analytic sense, but
*practically* continuous, as already explained. This means that it not only presents no absolute hiatus, but
that it has neither salients nor reentrants too acute or too accentuated.

And what gives us the right to make this hypothesis? We have already said it is because, since the beginning of the ages, there have always been complex causes ceaselessly acting in the same way and making the world tend toward uniformity without ever being able to turn back. These are the causes which little by little have flattened the salients and filled up the reentrants, and this is why our probability curves now show only gentle undulations. In milliards of milliards of ages another step will have been made toward uniformity, and these undulations will be ten times as gentle; the radius of mean curvature of our curve will have become ten times as great. And then such a length as seems to us to-day not very small, since on our curve an arc of this length can not be regarded as rectilineal, should on the contrary at that epoch be called very little, since the curvature will have become ten times less and an arc of this length may be sensibly identified with a sect.

Thus the phrase ‘very slight’ remains relative; but it is not relative to such or such a man, it is relative to the actual state of the world. It will change its meaning when the world shall have become more uniform, when all things shall have blended still more. But then doubtless men can no longer live and must give place to other beings — should I say far smaller or far larger? So that our criterion, remaining true for all men, retains an objective sense.

And on the other hand what means the phrase ‘very complex’? I have already given one solution, but there are others. Complex causes we have said produce a blend more and more intimate, but after how long a time will this blend satisfy us? When will it have accumulated sufficient complexity? When shall we have sufficiently shuffled the cards? If we mix two powders, one blue, the other white, there comes a moment when the tint of the mixture seems to us uniform because of the feebleness of our senses; it will be uniform for the presbyte, forced to gaze from afar, before it will be so for the myope. And when it has become uniform for all eyes, we still could push back the limit by the use of instruments. There is no chance for any man ever to discern the infinite variety which, if the kinetic theory is true, hides under the uniform appearance of a gas. And yet if we accept Gouy’s ideas on the Brownian movement, does not the microscope seem on the point of showing us something analogous?

This new criterion is therefore relative like the first; and if it retains an objective character, it is because all men have approximately the same senses, the power of their instruments is limited, and besides they use them only exceptionally.

It is just the same in the moral sciences and particularly in history. The historian is obliged to make a choice among the events of the epoch he studies; he recounts only those which seem to him the most important. He therefore contents himself with relating the most momentous events of the sixteenth century, for example, as likewise the most remarkable facts of the seventeenth century. If the first suffice to explain the second, we say these conform to the laws of history. But if a great event of the seventeenth century should have for cause a small fact of the sixteenth century which no history reports, which all the world has neglected, then we say this event is due to chance. This word has therefore the same sense as in the physical sciences; it means that slight causes have produced great effects.

The greatest bit of chance is the birth of a great man. It is only by chance that meeting of two germinal cells, of different sex, containing precisely, each on its side, the mysterious elements whose mutual reaction must produce the genius. One will agree that these elements must be rare and that their meeting is still more rare. How slight a thing it would have required to deflect from its route the carrying spermatozoon. It would have sufficed to deflect it a tenth of a millimeter and Napoleon would not have been born and the destinies of a continent would have been changed. No example can better make us understand the veritable characteristics of chance.

One more word about the paradoxes brought out by the application of the calculus of probabilities to the moral sciences. It has been proven that no Chamber of Deputies will ever fail to contain a member of the opposition, or at least such an event would be so improbable that we might without fear wager the contrary, and bet a million against a sou.

Condorcet has striven to calculate how many jurors it would require to make a judicial error practically impossible. If we had used the results of this calculation, we should certainly have been exposed to the same disappointments as in betting, on the faith of the calculus, that the opposition would never be without a representative.

The laws of chance do not apply to these questions. If justice be not always meted out to accord with the best reasons, it uses less than we think the method of Bridoye. This is perhaps to be regretted, for then the system of Condorcet would shield us from judicial errors.

What is the meaning of this? We are tempted to attribute facts of this nature to chance because their causes are obscure; but this is not true chance. The causes are unknown to us, it is true, and they are even complex; but they are not sufficiently so, since they conserve something. We have seen that this it is which distinguishes causes ‘too simple.’ When men are brought together they no longer decide at random and independently one of another; they influence one another. Multiplex causes come into action. They worry men, dragging them to right or left, but one thing there is they can not destroy, this is their Panurge flock-of-sheep habits. And this is an invariant.

Difficulties are indeed involved in the application of the calculus of probabilities to the exact sciences. Why are the decimals of a table of logarithms, why are those of the number π distributed in accordance with the laws of chance? Elsewhere I have already studied the question in so far as it concerns logarithms, and there it is easy. It is clear that a slight difference of argument will give a slight difference of logarithm, but a great difference in the sixth decimal of the logarithm. Always we find again the same criterion.

But as for the number π, that presents more difficulties, and I have at the moment nothing worth while to say.

There would be many other questions to resolve, had I wished to attack them before solving that which I more specially set myself. When we reach a simple result, when we find for example a round number, we say that such a result can not be due to chance, and we seek, for its explanation, a non-fortuitous cause. And in fact there is only a very slight probability that among 10,000 numbers chance will give a round number; for example, the number 10,000. This has only one chance in 10,000. But there is only one chance in 10,000 for the occurrence of any other one number; and yet this result will not astonish us, nor will it be hard for us to attribute it to chance; and that simply because it will be less striking.

Is this a simple illusion of ours, or are there cases where this way of thinking is legitimate? We must hope so, else were all science impossible. When we wish to check a hypothesis, what do we do? We can not verify all its consequences, since they would be infinite in number; we content ourselves with verifying certain ones and if we succeed we declare the hypothesis confirmed, because so much success could not be due to chance. And this is always at bottom the same reasoning.

I can not completely justify it here, since it would take too much time; but I may at least say that we find ourselves confronted by two hypotheses, either a simple cause or that aggregate of complex causes we call chance. We find it natural to suppose that the first should produce a simple result, and then, if we find that simple result, the round number for example, it seems more likely to us to be attributable to the simple cause which must give it almost certainly, than to chance which could only give it once in 10,000 times. It will not be the same if we find a result which is not simple; chance, it is true, will not give this more than once in 10,000 times; but neither has the simple cause any more chance of producing it.

Mathematical Reasoning

It is impossible to represent to oneself empty space; all our efforts to imagine a pure space, whence should be excluded the changing images of material objects, can result only in a representation where vividly colored surfaces, for example, are replaced by lines of faint coloration, and we can not go to the very end in this way without all vanishing and terminating in nothingness. Thence comes the irreducible relativity of space.

Whoever speaks of absolute space uses a meaningless phrase. This is a truth long proclaimed by all who have reflected upon the matter, but which we are too often led to forget.

I am at a determinate point in Paris, place du Panthéon for instance, and I say: I shall come back *here*
to-morrow. If I be asked: Do you mean you will return to the same point of space, I shall be tempted to answer: yes;
and yet I shall be wrong, since by to-morrow the earth will have journeyed hence, carrying with it the place du
Panthéon, which will have traveled over more than two million kilometers. And if I tried to speak more precisely, I
should gain nothing, since our globe has run over these two million kilometers in its motion with relation to the sun,
while the sun in its turn is displaced with reference to the Milky Way, while the Milky Way itself is doubtless in
motion without our being able to perceive its velocity. So that we are completely ignorant, and always shall be, of how
much the place du Panthéon is displaced in a day.

In sum, I meant to say: To-morrow I shall see again the dome and the pediment of the Panthéon, and if there were no Panthéon my phrase would be meaningless and space would vanish.

This is one of the most commonplace forms of the principle of the relativity of space; but there is another, upon
which Delbeuf has particularly insisted. Suppose that in the night all the dimensions of the universe become a thousand
times greater: the world will have remained *similar* to itself, giving to the word *similitude* the same
meaning as in Euclid, Book VI. Only what was a meter long will measure thenceforth a kilometer, what was a millimeter
long will become a meter. The bed whereon I lie and my body itself will be enlarged in the same proportion.

When I awake to-morrow morning, what sensation shall I feel in presence of such an astounding transformation? Well, I shall perceive nothing at all. The most precise measurements will be incapable of revealing to me anything of this immense convulsion, since the measures I use will have varied precisely in the same proportion as the objects I seek to measure. In reality, this convulsion exists only for those who reason as if space were absolute. If I for a moment have reasoned as they do, it is the better to bring out that their way of seeing implies contradiction. In fact it would be better to say that, space being relative, nothing at all has happened, which is why we have perceived nothing.

Has one the right, therefore, to say he knows the distance between two points? No, since this distance could undergo enormous variations without our being able to perceive them, provided the other distances have varied in the same proportion. We have just seen that when I say: I shall be here to-morrow, this does not mean: To-morrow I shall be at the same point of space where I am to-day, but rather: To-morrow I shall be at the same distance from the Panthéon as to-day. And we see that this statement is no longer sufficient and that I should say: To-morrow and to-day my distance from the Panthéon will be equal to the same number of times the height of my body.

But this is not all; I have supposed the dimensions of the world to vary, but that at least the world remained always similar to itself. We might go much further, and one of the most astonishing theories of modern physics furnishes us the occasion.

According to Lorentz and Fitzgerald, all the bodies borne along in the motion of the earth undergo a deformation.

This deformation is, in reality, very slight, since all dimensions parallel to the movement of the earth diminish by a hundred millionth, while the dimensions perpendicular to this movement are unchanged. But it matters little that it is slight, that it exists suffices for the conclusion I am about to draw. And besides, I have said it was slight, but in reality I know nothing about it; I have myself been victim of the tenacious illusion which makes us believe we conceive an absolute space; I have thought of the motion of the earth in its elliptic orbit around the sun, and I have allowed thirty kilometers as its velocity. But its real velocity (I mean, this time, not its absolute velocity, which is meaningless, but its velocity with relation to the ether), I do not know that, and have no means of knowing it: it is perhaps, 10, 100 times greater, and then the deformation will be 100, 10,000 times more.

Can we show this deformation? Evidently not; here is a cube with edge one meter; in consequence of the earth’s displacement it is deformed, one of its edges, that parallel to the motion, becomes smaller, the others do not change. If I wish to assure myself of it by aid of a meter measure, I shall measure first one of the edges perpendicular to the motion and shall find that my standard meter fits this edge exactly; and in fact neither of these two lengths is changed, since both are perpendicular to the motion. Then I wish to measure the other edge, that parallel to the motion; to do this I displace my meter and turn it so as to apply it to the edge. But the meter, having changed orientation and become parallel to the motion, has undergone, in its turn, the deformation, so that though the edge be not a meter long, it will fit exactly, I shall find out nothing.

You ask then of what use is the hypothesis of Lorentz and of Fitzgerald if no experiment can permit of its verification? It is my exposition that has been incomplete; I have spoken only of measurements that can be made with a meter; but we can also measure a length by the time it takes light to traverse it, on condition we suppose the velocity of light constant and independent of direction. Lorentz could have accounted for the facts by supposing the velocity of light greater in the direction of the earth’s motion than in the perpendicular direction. He preferred to suppose that the velocity is the same in these different directions but that the bodies are smaller in the one than in the other. If the wave surfaces of light had undergone the same deformations as the material bodies we should never have perceived the Lorentz-Fitzgerald deformation.

In either case, it is not a question of absolute magnitude, but of the measure of this magnitude by means of some instrument; this instrument may be a meter, or the path traversed by light; it is only the relation of the magnitude to the instrument that we measure; and if this relation is altered, we have no way of knowing whether it is the magnitude or the instrument which has changed.

But what I wish to bring out is, that in this deformation the world has not remained similar to itself; squares have become rectangles, circles ellipses, spheres ellipsoids. And yet we have no way of knowing whether this deformation be real.

Evidently one could go much further: in place of the Lorentz-Fitzgerald deformation, whose laws are particularly simple, we could imagine any deformation whatsoever. Bodies could be deformed according to any laws, as complicated as we might wish, we never should notice it provided all bodies without exception were deformed according to the same laws. In saying, all bodies without exception, I include of course our own body and the light rays emanating from different objects.

If we look at the world in one of those mirrors of complicated shape which deform objects in a bizarre way, the mutual relations of the different parts of this world would not be altered; if, in fact two real objects touch, their images likewise seem to touch. Of course when we look in such a mirror we see indeed the deformation, but this is because the real world subsists alongside of its deformed image; and then even were this real world hidden from us, something there is could not be hidden, ourself; we could not cease to see, or at least to feel, our body and our limbs which have not been deformed and which continue to serve us as instruments of measure.

But if we imagine our body itself deformed in the same way as if seen in the mirror, these instruments of measure in their turn will fail us and the deformation will no longer be ascertainable.

Consider in the same way two worlds images of one another; to each object *P* of the world *A*
corresponds in the world *B* an object *P´*, its image; the coordinates of this image *P´* are
determinate functions of those of the object *P*; moreover these functions may be any whatsoever; I only suppose
them chosen once for all. Between the position of *P* and that of *P´* there is a constant relation; what
this relation is, matters not; enough that it be constant.

Well, these two worlds will be indistinguishable one from the other. I mean the first will be for its inhabitants
what the second is for its. And so it will be as long as the two worlds remain strangers to each other. Suppose we
lived in world *A*, we shall have constructed our science and in particular our geometry; during this time the
inhabitants of world *B* will have constructed a science, and as their world is the image of ours, their
geometry will also be the image of ours or, better, it will be the same. But if for us some day a window is opened upon
world *B*, how we shall pity them: “Poor things,” we shall say, “they think they have made a geometry, but what
they call so is only a grotesque image of ours; their straights are all twisted, their circles are humped, their
spheres have capricious inequalities.” And we shall never suspect they say the same of us, and one never will know who
is right.

We see in how broad a sense should be understood the relativity of space; space is in reality amorphous and the
things which are therein alone give it a form. What then should be thought of that direct intuition we should have of
the straight or of distance? So little have we intuition of distance in itself that in the night, as we have said, a
distance might become a thousand times greater without our being able to perceive it, if all other distances had
undergone the same alteration. And even in a night the world *B* might be substituted for the world *A*
without our having any way of knowing it, and then the straight lines of yesterday would have ceased to be straight and
we should never notice.

One part of space is not by itself and in the absolute sense of the word equal to another part of space; because if
so it is for us, it would not be for the dwellers in world *B*; and these have just as much right to reject our
opinion as we to condemn theirs.

I have elsewhere shown what are the consequences of these facts from the viewpoint of the idea we should form of non-Euclidean geometry and other analogous geometries; to that I do not care to return; and to-day I shall take a somewhat different point of view.

If this intuition of distance, of direction, of the straight line, if this direct intuition of space in a word does not exist, whence comes our belief that we have it? If this is only an illusion, why is this illusion so tenacious? It is proper to examine into this. We have said there is no direct intuition of size and we can only arrive at the relation of this magnitude to our instruments of measure. We should therefore not have been able to construct space if we had not had an instrument to measure it; well, this instrument to which we relate everything, which we use instinctively, it is our own body. It is in relation to our body that we place exterior objects, and the only spatial relations of these objects that we can represent are their relations to our body. It is our body which serves us, so to speak, as system of axes of coordinates.

For example, at an instant α, the presence of the object *A* is revealed to me by the sense of sight; at
another instant, β, the presence of another object, *B*, is revealed to me by another sense, that of hearing or
of touch, for instance. I judge that this object *B* occupies the same place as the object *A*. What does
that mean? First that does not signify that these two objects occupy, at two different moments, the same point of an
absolute space, which even if it existed would escape our cognition, since, between the instants α and β, the solar
system has moved and we can not know its displacement. That means these two objects occupy the same relative position
with reference to our body.

But even this, what does it mean? The impressions that have come to us from these objects have followed paths
absolutely different, the optic nerve for the object *A*, the acoustic nerve for the
object *B*. They have nothing in common from the qualitative point of view. The representations we are able to
make of these two objects are absolutely heterogeneous, irreducible one to the other. Only I know that to reach the
object *A* I have just to extend the right arm in a certain way; even when I abstain from doing it, I represent
to myself the muscular sensations and other analogous sensations which would accompany this extension, and this
representation is associated with that of the object *A*.

Now, I likewise know I can reach the object *B* by extending my right arm in the same manner, an extension
accompanied by the same train of muscular sensations. And when I say these two objects occupy the same place, I mean
nothing more.

I also know I could have reached the object *A* by another appropriate motion of the left arm and I represent
to myself the muscular sensations which would have accompanied this movement; and by this same motion of the left arm,
accompanied by the same sensations, I likewise could have reached the object *B*.

And that is very important, since thus I can defend myself against dangers menacing me from the object *A* or
the object *B*. With each of the blows we can be hit, nature has associated one or more parries which permit of
our guarding ourselves. The same parry may respond to several strokes; and so it is, for instance, that the same motion
of the right arm would have allowed us to guard at the instant α against the object *A* and at the instant β
against the object *B*. Just so, the same stroke can be parried in several ways, and we have said, for instance,
the object *A* could be reached indifferently either by a certain movement of the right arm or by a certain
movement of the left arm.

All these parries have nothing in common except warding off the same blow, and this it is, and nothing else, which is meant when we say they are movements terminating at the same point of space. Just so, these objects, of which we say they occupy the same point of space, have nothing in common, except that the same parry guards against them.

Or, if you choose, imagine innumerable telegraph wires, some centripetal, others centrifugal. The centripetal wires warn us of accidents happening without; the centrifugal wires carry the reparation. Connections are so established that when a centripetal wire is traversed by a current this acts on a relay and so starts a current in one of the centrifugal wires, and things are so arranged that several centripetal wires may act on the same centrifugal wire if the same remedy suits several ills, and that a centripetal wire may agitate different centrifugal wires, either simultaneously or in lieu one of the other when the same ill may be cured by several remedies.

It is this complex system of associations, it is this table of distribution, so to speak, which is all our geometry or, if you wish, all in our geometry that is instinctive. What we call our intuition of the straight line or of distance is the consciousness we have of these associations and of their imperious character.

And it is easy to understand whence comes this imperious character itself. An association will seem to us by so much the more indestructible as it is more ancient. But these associations are not, for the most part, conquests of the individual, since their trace is seen in the new-born babe: they are conquests of the race. Natural selection had to bring about these conquests by so much the more quickly as they were the more necessary.

On this account, those of which we speak must have been of the earliest in date, since without them the defense of the organism would have been impossible. From the time when the cellules were no longer merely juxtaposed, but were called upon to give mutual aid, it was needful that a mechanism organize analogous to what we have described, so that this aid miss not its way, but forestall the peril.

When a frog is decapitated, and a drop of acid is placed on a point of its skin, it seeks to wipe off the acid with the nearest foot, and, if this foot be amputated, it sweeps it off with the foot of the opposite side. There we have the double parry of which I have just spoken, allowing the combating of an ill by a second remedy, if the first fails. And it is this multiplicity of parries, and the resulting coordination, which is space.

We see to what depths of the unconscious we must descend to find the first traces of these spatial associations, since only the inferior parts of the nervous system are involved. Why be astonished then at the resistance we oppose to every attempt made to dissociate what so long has been associated? Now, it is just this resistance that we call the evidence for the geometric truths; this evidence is nothing but the repugnance we feel toward breaking with very old habits which have always proved good.

The space so created is only a little space extending no farther than my arm can reach; the intervention of the memory is necessary to push back its limits. There are points which will remain out of my reach, whatever effort I make to stretch forth my hand; if I were fastened to the ground like a hydra polyp, for instance, which can only extend its tentacles, all these points would be outside of space, since the sensations we could experience from the action of bodies there situated, would be associated with the idea of no movement allowing us to reach them, of no appropriate parry. These sensations would not seem to us to have any spatial character and we should not seek to localize them.

But we are not fixed to the ground like the lower animals; we can, if the enemy be too far away, advance toward him first and extend the hand when we are sufficiently near. This is still a parry, but a parry at long range. On the other hand, it is a complex parry, and into the representation we make of it enter the representation of the muscular sensations caused by the movements of the legs, that of the muscular sensations caused by the final movement of the arm, that of the sensations of the semicircular canals, etc. We must, besides, represent to ourselves, not a complex of simultaneous sensations, but a complex of successive sensations, following each other in a determinate order, and this is why I have just said the intervention of memory was necessary. Notice moreover that, to reach the same point, I may approach nearer the mark to be attained, so as to have to stretch my arm less. What more? It is not one, it is a thousand parries I can oppose to the same danger. All these parries are made of sensations which may have nothing in common and yet we regard them as defining the same point of space, since they may respond to the same danger and are all associated with the notion of this danger. It is the potentiality of warding off the same stroke which makes the unity of these different parries, as it is the possibility of being parried in the same way which makes the unity of the strokes so different in kind, which may menace us from the same point of space. It is this double unity which makes the individuality of each point of space, and, in the notion of point, there is nothing else.

The space before considered, which might be called *restricted space*, was referred to coordinate axes bound
to my body; these axes were fixed, since my body did not move and only my members were displaced. What are the axes to
which we naturally refer the *extended space*? that is to say the new space just defined. We define a point by
the sequence of movements to be made to reach it, starting from a certain initial position of the body. The axes are
therefore fixed to this initial position of the body.

But the position I call initial may be arbitrarily chosen among all the positions my body has successively occupied; if the memory more or less unconscious of these successive positions is necessary for the genesis of the notion of space, this memory may go back more or less far into the past. Thence results in the definition itself of space a certain indetermination, and it is precisely this indetermination which constitutes its relativity.

There is no absolute space, there is only space relative to a certain initial position of the body. For a conscious
being fixed to the ground like the lower animals, and consequently knowing only restricted space, space would still be
relative (since it would have reference to his body), but this being would not be conscious of this relativity, because
the axes of reference for this restricted space would be unchanging! Doubtless the rock to which this being would be
fettered would not be motionless, since it would be carried along in the movement of our planet; for us consequently
these axes would change at each instant; but for him they would be changeless. We have the faculty of referring our
extended space now to the position *A* of our body, considered as initial, again to the position *B*,
which it had some moments afterward, and which we are free to regard in its turn as initial; we make therefore at each
instant unconscious transformations of coordinates. This faculty would be lacking in our imaginary being, and from not having traveled, he would think space absolute. At every instant, his system of
axes would be imposed upon him; this system would have to change greatly in reality, but for him it would be always the
same, since it would be always the *only* system. Quite otherwise is it with us, who at each instant have many
systems between which we may choose at will, on condition of going back by memory more or less far into the past.

This is not all; restricted space would not be homogeneous; the different points of this space could not be regarded as equivalent, since some could be reached only at the cost of the greatest efforts, while others could be easily attained. On the contrary, our extended space seems to us homogeneous, and we say all its points are equivalent. What does that mean?

If we start from a certain place *A*, we can, from this position, make certain movements, *M*,
characterized by a certain complex of muscular sensations. But, starting from another position, *B*, we make
movements *M´* characterized by the same muscular sensations. Let *a*, then, be the situation of a
certain point of the body, the end of the index finger of the right hand for example, in the initial position
*A*, and *b* the situation of this same index when, starting from this position *A*, we have made
the motions *M*. Afterwards, let *a´* be the situation of this index in the position *B*, and
*b´* its situation when, starting from the position *B*, we have made the motions *M´*.

Well, I am accustomed to say that the points of space *a* and *b* are related to each other just as
the points *a´* and *b´*, and this simply means that the two series of movements *M* and
*M´* are accompanied by the same muscular sensations. And as I am conscious that, in passing from the position
*A* to the position *B*, my body has remained capable of the same movements, I know there is a point of
space related to the point *a´* just as any point *b* is to the point *a*, so that the two points
*a* and *a´* are equivalent. This is what is called the homogeneity of space. And, at the same time, this
is why space is relative, since its properties remain the same whether it be referred to the axes *A* or to the
axes *B*. So that the relativity of space and its homogeneity are one sole and same thing.

Now, if I wish to pass to the great space, which no longer serves only for me, but where I may lodge the universe, I get there by an act of imagination. I imagine how a giant would feel who could reach the planets in a few steps; or, if you choose, what I myself should feel in presence of a miniature world where these planets were replaced by little balls, while on one of these little balls moved a liliputian I should call myself. But this act of imagination would be impossible for me had I not previously constructed my restricted space and my extended space for my own use.

Why now have all these spaces three dimensions? Go back to the “table of distribution” of which we have spoken. We
have on the one side the list of the different possible dangers; designate them by *A1*, *A2*, etc.; and,
on the other side, the list of the different remedies which I shall call in the same way *B1*, *B2*, etc.
We have then connections between the contact studs or push buttons of the first list and those of the second, so that
when, for instance, the announcer of danger *A3* functions, it will put or may put in action the relay
corresponding to the parry *B4*.

As I have spoken above of centripetal or centrifugal wires, I fear lest one see in all this, not a simple comparison, but a description of the nervous system. Such is not my thought, and that for several reasons: first I should not permit myself to put forth an opinion on the structure of the nervous system which I do not know, while those who have studied it speak only circumspectly; again because, despite my incompetence, I well know this scheme would be too simplistic; and finally because on my list of parries, some would figure very complex, which might even, in the case of extended space, as we have seen above, consist of many steps followed by a movement of the arm. It is not a question then of physical connection between two real conductors but of psychologic association between two series of sensations.

If *A1* and *A2* for instance are both associated with the parry *B1*, and if *A1* is
likewise associated with the parry *B2*, it will generally happen that *A2* and *B2* will also
themselves be associated. If this fundamental law were not generally true, there would exist
only an immense confusion and there would be nothing resembling a conception of space or a geometry. How in fact have
we defined a point of space. We have done it in two ways: it is on the one hand the aggregate of announcers *A*
in connection with the same parry *B*; it is on the other hand the aggregate of parries *B* in connection
with the same announcer *A*. If our law was not true, we should say *A1* and *A2* correspond to
the same point since they are both in connection with *B1*; but we should likewise say they do not correspond to
the same point, since *A1* would be in connection with *B2* and the same would not be true of
*A2*. This would be a contradiction.

But, from another side, if the law were rigorously and always true, space would be very different from what it is.
We should have categories strongly contrasted between which would be portioned out on the one hand the announcers
*A*, on the other hand the parries *B*; these categories would be excessively numerous, but they would be
entirely separated one from another. Space would be composed of points very numerous, but discrete; it would be
*discontinuous*. There would be no reason for ranging these points in one order rather than another, nor
consequently for attributing to space three dimensions.

But it is not so; permit me to resume for a moment the language of those who already know geometry; this is quite proper since this is the language best understood by those I wish to make understand me.

When I desire to parry the stroke, I seek to attain the point whence comes this blow, but it suffices that I
approach quite near. Then the parry *B1* may answer for *A1* and for *A2*, if the point which
corresponds to *B1* is sufficiently near both to that corresponding to *A1* and to that corresponding to
*A2*. But it may happen that the point corresponding to another parry *B2* may be sufficiently near to
the point corresponding to A1 and not sufficiently near the point corresponding to *A2*; so that the parry
*B2* may answer for *A1* without answering for *A2*. For one who does not yet know geometry, this
translates itself simply by a derogation of the law stated above. And then things will happen thus:

Two parries *B1* and *B2* will be associated with the same warning *A1*
and with a large number of warnings which we shall range in the same category as *A1* and which we shall make
correspond to the same point of space. But we may find warnings *A2* which will be associated with *B2*
without being associated with *B1*, and which in compensation will be associated with *B3*, which
*B3* was not associated with *A1*, and so forth, so that we may write the series

*B1*, *A1*, *B2*, *A2*, *B3*, *A3*, *B4*,
*A4*,

where each term is associated with the following and the preceding, but not with the terms several places away.

Needless to add that each of the terms of these series is not isolated, but forms part of a very numerous category of other warnings or of other parries which have the same connections as it, and which may be regarded as belonging to the same point of space.

The fundamental law, though admitting of exceptions, remains therefore almost always true. Only, in consequence of these exceptions, these categories, in place of being entirely separated, encroach partially one upon another and mutually penetrate in a certain measure, so that space becomes continuous.

On the other hand, the order in which these categories are to be ranged is no longer arbitrary, and if we refer to
the preceding series, we see it is necessary to put *B2* between *A1* and *A2* and consequently
between *B1* and *B3* and that we could not for instance put it between *B3* and *B4*.

There is therefore an order in which are naturally arranged our categories which correspond to the points of space, and experience teaches us that this order presents itself under the form of a table of triple entry, and this is why space has three dimensions.

So the characteristic property of space, that of having three dimensions, is only a property of our table of distribution, an internal property of the human intelligence, so to speak. It would suffice to destroy certain of these connections, that is to say of the associations of ideas to give a different table of distribution, and that might be enough for space to acquire a fourth dimension.

Some persons will be astonished at such a result. The external world, they will think, should count for something. If the number of dimensions comes from the way we are made, there might be thinking beings living in our world, but who might be made differently from us and who would believe space has more or less than three dimensions. Has not M. de Cyon said that the Japanese mice, having only two pair of semicircular canals, believe that space is two-dimensional? And then this thinking being, if he is capable of constructing a physics, would he not make a physics of two or of four dimensions, and which in a sense would still be the same as ours, since it would be the description of the same world in another language?

It seems in fact that it would be possible to translate our physics into the language of geometry of four
dimensions; to attempt this translation would be to take great pains for little profit, and I shall confine myself to
citing the mechanics of Hertz where we have something analogous. However, it seems that the translation would always be
less simple than the text, and that it would always have the air of a translation, that the language of three
dimensions seems the better fitted to the description of our world, although this description can be rigorously made in
another idiom. Besides, our table of distribution was not made at random. There is connection between the warning
*A1* and the parry *B1*, this is an internal property of our intelligence; but why this connection? It is
because the parry *B1* affords means effectively to guard against the danger *A1*; and this is a fact
exterior to us, this is a property of the exterior world. Our table of distribution is therefore only the translation
of an aggregate of exterior facts; if it has three dimensions, this is because it has adapted itself to a world having
certain properties; and the chief of these properties is that there exist natural solids whose displacements follow
sensibly the laws we call laws of motion of rigid solids. If therefore the language of three dimensions is that which
permits us most easily to describe our world, we should not be astonished; this language is copied from our table of
distribution; and it is in order to be able to live in this world that this table has been established.

I have said we could conceive, living in our world, thinking beings whose table of distribution would be four-dimensional and who consequently would think in hyperspace. It is not certain however that such beings, admitting they were born there, could live there and defend themselves against the thousand dangers by which they would there be assailed.

A few remarks to end with. There is a striking contrast between the roughness of this primitive geometry, reducible to what I call a table of distribution, and the infinite precision of the geometers’ geometry. And yet this is born of that; but not of that alone; it must be made fecund by the faculty we have of constructing mathematical concepts, such as that of group, for instance; it was needful to seek among the pure concepts that which best adapts itself to this rough space whose genesis I have sought to explain and which is common to us and the higher animals.

The evidence for certain geometric postulates, we have said, is only our repugnance to renouncing very old habits. But these postulates are infinitely precise, while these habits have something about them essentially pliant. When we wish to think, we need postulates infinitely precise, since this is the only way to avoid contradiction; but among all the possible systems of postulates, there are some we dislike to choose because they are not sufficiently in accord with our habits; however pliant, however elastic they may be, these have a limit of elasticity.

We see that if geometry is not an experimental science, it is a science born apropos of experience; that we have created the space it studies, but adapting it to the world wherein we live. We have selected the most convenient space, but experience has guided our choice; as this choice has been unconscious, we think it has been imposed upon us; some say experience imposes it, others that we are born with our space ready made; we see from the preceding considerations, what in these two opinions is the part of truth, what of error.

In this progressive education whose outcome has been the construction of space, it is very difficult to determine what is the part of the individual, what the part of the race. How far could one of us, transported from birth to an entirely different world, where were dominant, for instance, bodies moving in conformity to the laws of motion of non-Euclidean solids, renounce the ancestral space to build a space completely new?

The part of the race seems indeed preponderant; yet if to it we owe rough space, the soft space I have spoken of,
the space of the higher animals, is it not to the unconscious experience of the individual we owe the infinitely
precise space of the geometer? This is a question not easy to solve. Yet we cite a fact showing that the space our
ancestors have bequeathed us still retains a certain plasticity. Some hunters learn to shoot fish under water, though
the image of these fish be turned up by refraction. Besides they do it instinctively: they therefore have learned to
modify their old instinct of direction; or, if you choose, to substitute for the association *A1*, *B1*,
another association *A1*, *B2*, because experience showed them the first would not work.

1. I should speak here of general definitions in mathematics; at least that is the title, but it will be impossible to confine myself to the subject as strictly as the rule of unity of action would require; I shall not be able to treat it without touching upon a few other related questions, and if thus I am forced from time to time to walk on the bordering flower-beds on the right or left, I pray you bear with me.

What is a good definition? For the philosopher or the scientist it is a definition which applies to all the objects defined, and only those; it is the one satisfying the rules of logic. But in teaching it is not that; a good definition is one understood by the scholars.

How does it happen that so many refuse to understand mathematics? Is that not something of a paradox? Lo and behold! a science appealing only to the fundamental principles of logic, to the principle of contradiction, for instance, to that which is the skeleton, so to speak, of our intelligence, to that of which we can not divest ourselves without ceasing to think, and there are people who find it obscure! and they are even in the majority! That they are incapable of inventing may pass, but that they do not understand the demonstrations shown them, that they remain blind when we show them a light which seems to us flashing pure flame, this it is which is altogether prodigious.

And yet there is no need of a wide experience with examinations to know that these blind men are in no wise exceptional beings. This is a problem not easy to solve, but which should engage the attention of all those wishing to devote themselves to teaching.

What is it, to understand? Has this word the same meaning for all the world? To understand the demonstration of a theorem, is that to examine successively each of the syllogisms composing it and to ascertain its correctness, its conformity to the rules of the game? Likewise, to understand a definition, is this merely to recognize that one already knows the meaning of all the terms employed and to ascertain that it implies no contradiction?

For some, yes; when they have done this, they will say: I understand.

For the majority, no. Almost all are much more exacting; they wish to know not merely whether all the syllogisms of a demonstration are correct, but why they link together in this order rather than another. In so far as to them they seem engendered by caprice and not by an intelligence always conscious of the end to be attained, they do not believe they understand.

Doubtless they are not themselves just conscious of what they crave and they could not formulate their desire, but if they do not get satisfaction, they vaguely feel that something is lacking. Then what happens? In the beginning they still perceive the proofs one puts under their eyes; but as these are connected only by too slender a thread to those which precede and those which follow, they pass without leaving any trace in their head; they are soon forgotten; a moment bright, they quickly vanish in night eternal. When they are farther on, they will no longer see even this ephemeral light, since the theorems lean one upon another and those they would need are forgotten; thus it is they become incapable of understanding mathematics.

This is not always the fault of their teacher; often their mind, which needs to perceive the guiding thread, is too lazy to seek and find it. But to come to their aid, we first must know just what hinders them.

Others will always ask of what use is it; they will not have understood if they do not find about them, in practise or in nature, the justification of such and such a mathematical concept. Under each word they wish to put a sensible image; the definition must evoke this image, so that at each stage of the demonstration they may see it transform and evolve. Only upon this condition do they comprehend and retain. Often these deceive themselves; they do not listen to the reasoning, they look at the figures; they think they have understood and they have only seen.

2. How many different tendencies! Must we combat them? Must we use them? And if we wish to combat them, which should be favored? Must we show those content with the pure logic that they have seen only one side of the matter? Or need we say to those not so cheaply satisfied that what they demand is not necessary?

In other words, should we constrain the young people to change the nature of their minds? Such an attempt would be vain; we do not possess the philosopher’s stone which would enable us to transmute one into another the metals confided to us; all we can do is to work with them, adapting ourselves to their properties.

Many children are incapable of becoming mathematicians, to whom however it is necessary to teach mathematics; and the mathematicians themselves are not all cast in the same mold. To read their works suffices to distinguish among them two sorts of minds, the logicians like Weierstrass for example, the intuitives like Riemann. There is the same difference among our students. The one sort prefer to treat their problems ‘by analysis’ as they say, the others ‘by geometry.’

It is useless to seek to change anything of that, and besides would it be desirable? It is well that there are logicians and that there are intuitives; who would dare say whether he preferred that Weierstrass had never written or that there never had been a Riemann? We must therefore resign ourselves to the diversity of minds, or better we must rejoice in it.

3. Since the word understand has many meanings, the definitions which will be best understood by some will not be best suited to others. We have those which seek to produce an image, and those where we confine ourselves to combining empty forms, perfectly intelligible, but purely intelligible, which abstraction has deprived of all matter.

I know not whether it be necessary to cite examples. Let us cite them, anyhow, and first the definition of fractions will furnish us an extreme case. In the primary schools, to define a fraction, one cuts up an apple or a pie; it is cut up mentally of course and not in reality, because I do not suppose the budget of the primary instruction allows of such prodigality. At the Normal School, on the other hand, or at the college, it is said: a fraction is the combination of two whole numbers separated by a horizontal bar; we define by conventions the operations to which these symbols may be submitted; it is proved that the rules of these operations are the same as in calculating with whole numbers, and we ascertain finally that multiplying the fraction, according to these rules, by the denominator gives the numerator. This is all very well because we are addressing young people long familiarized with the notion of fractions through having cut up apples or other objects, and whose mind, matured by a hard mathematical education, has come little by little to desire a purely logical definition. But the débutant to whom one should try to give it, how dumfounded!

Such also are the definitions found in a book justly admired and greatly honored, the *Foundations of
Geometry* by Hilbert. See in fact how he begins: *We think three systems of* things *which we shall call points, straights and planes*. What are these ‘things’?

We know not, nor need we know; it would even be a pity to seek to know; all we have the right to know of them is
what the assumptions tell us; this for example: *Two distinct points always determine a straight*, which is
followed by this remark: *in place of determine, we may say the two points are on the straight, or the straight goes
through these two points or joins the two points*.

Thus ‘to be on a straight’ is simply defined as synonymous with ‘determine a straight.’ Behold a book of which I think much good, but which I should not recommend to a school boy. Yet I could do so without fear, he would not read much of it. I have taken extreme examples and no teacher would dream of going that far. But even stopping short of such models, does he not already expose himself to the same danger?

Suppose we are in a class; the professor dictates: the circle is the locus of points of the plane equidistant from an interior point called the center. The good scholar writes this phrase in his note-book; the bad scholar draws faces; but neither understands; then the professor takes the chalk and draws a circle on the board. “Ah!” think the scholars, “why did he not say at once: a circle is a ring, we should have understood.” Doubtless the professor is right. The scholars’ definition would have been of no avail, since it could serve for no demonstration, since besides it would not give them the salutary habit of analyzing their conceptions. But one should show them that they do not comprehend what they think they know, lead them to be conscious of the roughness of their primitive conception, and of themselves to wish it purified and made precise.

4. I shall return to these examples; I only wished to show you the two opposed conceptions; they are in violent contrast. This contrast the history of science explains. If we read a book written fifty years ago, most of the reasoning we find there seems lacking in rigor. Then it was assumed a continuous function can change sign only by vanishing; to-day we prove it. It was assumed the ordinary rules of calculation are applicable to incommensurable numbers; to-day we prove it. Many other things were assumed which sometimes were false.

We trusted to intuition; but intuition can not give rigor, nor even certainty; we see this more and more. It tells us for instance that every curve has a tangent, that is to say that every continuous function has a derivative, and that is false. And as we sought certainty, we had to make less and less the part of intuition.

What has made necessary this evolution? We have not been slow to perceive that rigor could not be established in the reasonings, if it were not first put into the definitions.

The objects occupying mathematicians were long ill defined; we thought we knew them because we represented them with the senses or the imagination; but we had of them only a rough image and not a precise concept upon which reasoning could take hold. It is there that the logicians would have done well to direct their efforts.

So for the incommensurable number, the vague idea of continuity, which we owe to intuition, has resolved itself into a complicated system of inequalities bearing on whole numbers. Thus have finally vanished all those difficulties which frightened our fathers when they reflected upon the foundations of the infinitesimal calculus. To-day only whole numbers are left in analysis, or systems finite or infinite of whole numbers, bound by a plexus of equalities and inequalities. Mathematics we say is arithmetized.

5. But do you think mathematics has attained absolute rigor without making any sacrifice? Not at all; what it has gained in rigor it has lost in objectivity. It is by separating itself from reality that it has acquired this perfect purity. We may freely run over its whole domain, formerly bristling with obstacles, but these obstacles have not disappeared. They have only been moved to the frontier, and it would be necessary to vanquish them anew if we wished to break over this frontier to enter the realm of the practical.

We had a vague notion, formed of incongruous elements, some *a priori*, others coming from experiences more
or less digested; we thought we knew, by intuition, its principal properties. To-day we reject the empiric elements,
retaining only the *a priori*; one of the properties serves as definition and all the others are deduced from it
by rigorous reasoning. This is all very well, but it remains to be proved that this property, which has become a
definition, pertains to the real objects which experience had made known to us and whence we drew our vague intuitive
notion. To prove that, it would be necessary to appeal to experience, or to make an effort of intuition, and if we
could not prove it, our theorems would be perfectly rigorous, but perfectly useless.

Logic sometimes makes monsters. Since half a century we have seen arise a crowd of bizarre functions which seem to try to resemble as little as possible the honest functions which serve some purpose. No longer continuity, or perhaps continuity, but no derivatives, etc. Nay more, from the logical point of view, it is these strange functions which are the most general, those one meets without seeking no longer appear except as particular case. There remains for them only a very small corner.

Heretofore when a new function was invented, it was for some practical end; to-day they are invented expressly to put at fault the reasonings of our fathers, and one never will get from them anything more than that.

If logic were the sole guide of the teacher, it would be necessary to begin with the most general functions, that is to say with the most bizarre. It is the beginner that would have to be set grappling with this teratologic museum. If you do not do it, the logicians might say, you will achieve rigor only by stages.

6. Yes, perhaps, but we can not make so cheap of reality, and I mean not only the reality of the sensible world, which however has its worth, since it is to combat against it that nine tenths of your students ask of you weapons. There is a reality more subtile, which makes the very life of the mathematical beings, and which is quite other than logic.

Our body is formed of cells, and the cells of atoms; are these cells and these atoms then all the reality of the human body? The way these cells are arranged, whence results the unity of the individual, is it not also a reality and much more interesting?

A naturalist who never had studied the elephant except in the microscope, would he think he knew the animal adequately? It is the same in mathematics. When the logician shall have broken up each demonstration into a multitude of elementary operations, all correct, he still will not possess the whole reality; this I know not what which makes the unity of the demonstration will completely escape him.

In the edifices built up by our masters, of what use to admire the work of the mason if we can not comprehend the plan of the architect? Now pure logic can not give us this appreciation of the total effect; this we must ask of intuition.

Take for instance the idea of continuous function. This is at first only a sensible image, a mark traced by the
chalk on the blackboard. Little by little it is refined; we use it to construct a complicated system of inequalities,
which reproduces all the features of the primitive image; when all is done, we have *removed the centering*, as
after the construction of an arch; this rough representation, support thenceforth useless, has disappeared and there
remains only the edifice itself, irreproachable in the eyes of the logician. And yet, if the professor did not recall
the primitive image, if he did not restore momentarily the *centering*, how could the student divine by what
caprice all these inequalities have been scaffolded in this fashion one upon another? The definition would be logically
correct, but it would not show him the veritable reality.

7. So back we must return; doubtless it is hard for a master to teach what does not entirely satisfy him; but the satisfaction of the master is not the unique object of teaching; we should first give attention to what the mind of the pupil is and to what we wish it to become.

Zoologists maintain that the embryonic development of an animal recapitulates in brief the whole history of its ancestors throughout geologic time. It seems it is the same in the development of minds. The teacher should make the child go over the path his fathers trod; more rapidly, but without skipping stations. For this reason, the history of science should be our first guide.

Our fathers thought they knew what a fraction was, or continuity, or the area of a curved surface; we have found they did not know it. Just so our scholars think they know it when they begin the serious study of mathematics. If without warning I tell them: “No, you do not know it; what you think you understand, you do not understand; I must prove to you what seems to you evident,” and if in the demonstration I support myself upon premises which to them seem less evident than the conclusion, what shall the unfortunates think? They will think that the science of mathematics is only an arbitrary mass of useless subtilities; either they will be disgusted with it, or they will play it as a game and will reach a state of mind like that of the Greek sophists.

Later, on the contrary, when the mind of the scholar, familiarized with mathematical reasoning, has been matured by this long frequentation, the doubts will arise of themselves and then your demonstration will be welcome. It will awaken new doubts, and the questions will arise successively to the child, as they arose successively to our fathers, until perfect rigor alone can satisfy him. To doubt everything does not suffice, one must know why he doubts.

8. The principal aim of mathematical teaching is to develop certain faculties of the mind, and among them intuition is not the least precious. It is through it that the mathematical world remains in contact with the real world, and if pure mathematics could do without it, it would always be necessary to have recourse to it to fill up the chasm which separates the symbol from reality. The practician will always have need of it, and for one pure geometer there should be a hundred practicians.

The engineer should receive a complete mathematical education, but for what should it serve him?

To see the different aspects of things and see them quickly; he has no time to hunt mice. It is necessary that, in the complex physical objects presented to him, he should promptly recognize the point where the mathematical tools we have put in his hands can take hold. How could he do it if we should leave between instruments and objects the deep chasm hollowed out by the logicians?

9. Besides the engineers, other scholars, less numerous, are in their turn to become teachers; they therefore must go to the very bottom; a knowledge deep and rigorous of the first principles is for them before all indispensable. But this is no reason not to cultivate in them intuition; for they would get a false idea of the science if they never looked at it except from a single side, and besides they could not develop in their students a quality they did not themselves possess.

For the pure geometer himself, this faculty is necessary; it is by logic one demonstrates, by intuition one invents. To know how to criticize is good, to know how to create is better. You know how to recognize if a combination is correct; what a predicament if you have not the art of choosing among all the possible combinations. Logic tells us that on such and such a way we are sure not to meet any obstacle; it does not say which way leads to the end. For that it is necessary to see the end from afar, and the faculty which teaches us to see is intuition. Without it the geometer would be like a writer who should be versed in grammar but had no ideas. Now how could this faculty develop if, as soon as it showed itself, we chase it away and proscribe it, if we learn to set it at naught before knowing the good of it.

And here permit a parenthesis to insist upon the importance of written exercises. Written compositions are perhaps not sufficiently emphasized in certain examinations, at the polytechnic school, for instance. I am told they would close the door against very good scholars who have mastered the course, thoroughly understanding it, and who nevertheless are incapable of making the slightest application. I have just said the word understand has several meanings: such students only understand in the first way, and we have seen that suffices neither to make an engineer nor a geometer. Well, since choice must be made, I prefer those who understand completely.

10. But is the art of sound reasoning not also a precious thing, which the professor of mathematics ought before all to cultivate? I take good care not to forget that. It should occupy our attention and from the very beginning. I should be distressed to see geometry degenerate into I know not what tachymetry of low grade and I by no means subscribe to the extreme doctrines of certain German Oberlehrer. But there are occasions enough to exercise the scholars in correct reasoning in the parts of mathematics where the inconveniences I have pointed out do not present themselves. There are long chains of theorems where absolute logic has reigned from the very first and, so to speak, quite naturally, where the first geometers have given us models we should constantly imitate and admire.

It is in the exposition of first principles that it is necessary to avoid too much subtility; there it would be most discouraging and moreover useless. We can not prove everything and we can not define everything; and it will always be necessary to borrow from intuition; what does it matter whether it be done a little sooner or a little later, provided that in using correctly premises it has furnished us, we learn to reason soundly.

11. Is it possible to fulfill so many opposing conditions? Is this possible in particular when it is a question of giving a definition? How find a concise statement satisfying at once the uncompromising rules of logic, our desire to grasp the place of the new notion in the totality of the science, our need of thinking with images? Usually it will not be found, and this is why it is not enough to state a definition; it must be prepared for and justified.

What does that mean? You know it has often been said: every definition implies an assumption, since it affirms the
existence of the object defined. The definition then will not be justified, from the purely
logical point of view, until one shall have *proved* that it involves no contradiction, neither in the terms,
nor with the verities previously admitted.

But this is not enough; the definition is stated to us as a convention; but most minds will revolt if we wish to
impose it upon them as an *arbitrary* convention. They will be satisfied only when you have answered numerous
questions.

Usually mathematical definitions, as M. Liard has shown, are veritable constructions built up wholly of more simple notions. But why assemble these elements in this way when a thousand other combinations were possible?

Is it by caprice? If not, why had this combination more right to exist than all the others? To what need does it respond? How was it foreseen that it would play an important rôle in the development of the science, that it would abridge our reasonings and our calculations? Is there in nature some familiar object which is so to speak the rough and vague image of it?

This is not all; if you answer all these questions in a satisfactory manner, we shall see indeed that the new-born had the right to be baptized; but neither is the choice of a name arbitrary; it is needful to explain by what analogies one has been guided and that if analogous names have been given to different things, these things at least differ only in material and are allied in form; that their properties are analogous and so to say parallel.

At this cost we may satisfy all inclinations. If the statement is correct enough to please the logician, the justification will satisfy the intuitive. But there is still a better procedure; wherever possible, the justification should precede the statement and prepare for it; one should be led on to the general statement by the study of some particular examples.

Still another thing: each of the parts of the statement of a definition has as aim to distinguish the thing to be defined from a class of other neighboring objects. The definition will be understood only when you have shown, not merely the object defined, but the neighboring objects from which it is proper to distinguish it, when you have given a grasp of the difference and when you have added explicitly: this is why in stating the definition I have said this or that.

But it is time to leave generalities and examine how the somewhat abstract principles I have expounded may be applied in arithmetic, geometry, analysis and mechanics.

12. The whole number is not to be defined; in return, one ordinarily defines the operations upon whole numbers; I believe the scholars learn these definitions by heart and attach no meaning to them. For that there are two reasons: first they are made to learn them too soon, when their mind as yet feels no need of them; then these definitions are not satisfactory from the logical point of view. A good definition for addition is not to be found just simply because we must stop and can not define everything. It is not defining addition to say it consists in adding. All that can be done is to start from a certain number of concrete examples and say: the operation we have performed is called addition.

For subtraction it is quite otherwise; it may be logically defined as the operation inverse to addition; but should we begin in that way? Here also start with examples, show on these examples the reciprocity of the two operations; thus the definition will be prepared for and justified.

Just so again for multiplication; take a particular problem; show that it may be solved by adding several equal numbers; then show that we reach the result more quickly by a multiplication, an operation the scholars already know how to do by routine and out of that the logical definition will issue naturally.

Division is defined as the operation inverse to multiplication; but begin by an example taken from the familiar notion of partition and show on this example that multiplication reproduces the dividend.

There still remain the operations on fractions. The only difficulty is for multiplication. It is best to expound first the theory of proportion; from it alone can come a logical definition; but to make acceptable the definitions met at the beginning of this theory, it is necessary to prepare for them by numerous examples taken from classic problems of the rule of three, taking pains to introduce fractional data.

Neither should we fear to familiarize the scholars with the notion of proportion by geometric images, either by appealing to what they remember if they have already studied geometry, or in having recourse to direct intuition, if they have not studied it, which besides will prepare them to study it. Finally I shall add that after defining multiplication of fractions, it is needful to justify this definition by showing that it is commutative, associative and distributive, and calling to the attention of the auditors that this is established to justify the definition.

One sees what a rôle geometric images play in all this; and this rôle is justified by the philosophy and the history of the science. If arithmetic had remained free from all admixture of geometry, it would have known only the whole number; it is to adapt itself to the needs of geometry that it invented anything else.

In geometry we meet forthwith the notion of the straight line. Can the straight line be defined? The well-known
definition, the shortest path from one point to another, scarcely satisfies me. I should start simply with the
*ruler* and show at first to the scholar how one may verify a ruler by turning; this verification is the true
definition of the straight line; the straight line is an axis of rotation. Next he should be shown how to verify the
ruler by sliding and he would have one of the most important properties of the straight line.

As to this other property of being the shortest path from one point to another, it is a theorem which can be demonstrated apodictically, but the demonstration is too delicate to find a place in secondary teaching. It will be worth more to show that a ruler previously verified fits on a stretched thread. In presence of difficulties like these one need not dread to multiply assumptions, justifying them by rough experiments.

It is needful to grant these assumptions, and if one admits a few more of them than is strictly necessary, the evil is not very great; the essential thing is to learn to reason soundly on the assumptions admitted. Uncle Sarcey, who loved to repeat, often said that at the theater the spectator accepts willingly all the postulates imposed upon him at the beginning, but the curtain once raised, he becomes uncompromising on the logic. Well, it is just the same in mathematics.

For the circle, we may start with the compasses; the scholars will recognize at the first glance the curve traced; then make them observe that the distance of the two points of the instrument remains constant, that one of these points is fixed and the other movable, and so we shall be led naturally to the logical definition.

The definition of the plane implies an axiom and this need not be hidden. Take a drawing board and show that a moving ruler may be kept constantly in complete contact with this plane and yet retain three degrees of freedom. Compare with the cylinder and the cone, surfaces on which an applied straight retains only two degrees of freedom; next take three drawing boards; show first that they will glide while remaining applied to one another and this with three degrees of freedom; and finally to distinguish the plane from the sphere, show that two of these boards which fit a third will fit each other.

Perhaps you are surprised at this incessant employment of moving things; this is not a rough artifice; it is much more philosophic than one would at first think. What is geometry for the philosopher? It is the study of a group. And what group? That of the motions of solid bodies. How define this group then without moving some solids?

Should we retain the classic definition of parallels and say parallels are two coplanar straights which do not meet, however far they be prolonged? No, since this definition is negative, since it is unverifiable by experiment, and consequently can not be regarded as an immediate datum of intuition. No, above all because it is wholly strange to the notion of group, to the consideration of the motion of solid bodies which is, as I have said, the true source of geometry. Would it not be better to define first the rectilinear translation of an invariable figure, as a motion wherein all the points of this figure have rectilinear trajectories; to show that such a translation is possible by making a square glide on a ruler?

From this experimental ascertainment, set up as an assumption, it would be easy to derive the notion of parallel and Euclid’s postulate itself.

I need not return to the definition of velocity, or acceleration, or other kinematic notions; they may be advantageously connected with that of the derivative.

I shall insist, on the other hand, upon the dynamic notions of force and mass.

I am struck by one thing: how very far the young people who have received a high-school education are from applying to the real world the mechanical laws they have been taught. It is not only that they are incapable of it; they do not even think of it. For them the world of science and the world of reality are separated by an impervious partition wall.

If we try to analyze the state of mind of our scholars, this will astonish us less. What is for them the real definition of force? Not that which they recite, but that which, crouching in a nook of their mind, from there directs it wholly. Here is the definition: forces are arrows with which one makes parallelograms. These arrows are imaginary things which have nothing to do with anything existing in nature. This would not happen if they had been shown forces in reality before representing them by arrows.

How shall we define force?

I think I have elsewhere sufficiently shown there is no good logical definition. There is the anthropomorphic definition, the sensation of muscular effort; this is really too rough and nothing useful can be drawn from it.

Here is how we should go: first, to make known the genus force, we must show one after the other all the species of this genus; they are very numerous and very different; there is the pressure of fluids on the insides of the vases wherein they are contained; the tension of threads; the elasticity of a spring; the gravity working on all the molecules of a body; friction; the normal mutual action and reaction of two solids in contact.

This is only a qualitative definition; it is necessary to learn to measure force. For that begin by showing that one force may be replaced by another without destroying equilibrium; we may find the first example of this substitution in the balance and Borda’s double weighing.

Then show that a weight may be replaced, not only by another weight, but by force of a different nature; for instance, Prony’s brake permits replacing weight by friction.

From all this arises the notion of the equivalence of two forces.

The direction of a force must be defined. If a force *F* is equivalent to another force *F´* applied
to the body considered by means of a stretched string, so that *F* may be replaced by *F´* without
affecting the equilibrium, then the point of attachment of the string will be by definition the point of application of
the force *F´*, and that of the equivalent force *F*; the direction of the string will be the direction
of the force *F´* and that of the equivalent force *F*.

From that, pass to the comparison of the magnitude of forces. If a force can replace two others with the same direction, it equals their sum; show for example that a weight of 20 grams may replace two 10-gram weights.

Is this enough? Not yet. We now know how to compare the intensity of two forces which have the same direction and same point of application; we must learn to do it when the directions are different. For that, imagine a string stretched by a weight and passing over a pulley; we shall say that the tensor of the two legs of the string is the same and equal to the tension weight.

This definition of ours enables us to compare the tensions of the two pieces of our string, and, using the preceding definitions, to compare any two forces having the same direction as these two pieces. It should be justified by showing that the tension of the last piece of the string remains the same for the same tensor weight, whatever be the number and the disposition of the reflecting pulleys. It has still to be completed by showing this is only true if the pulleys are frictionless.

Once master of these definitions, it is to be shown that the point of application, the direction and the intensity
suffice to determine a force; that two forces for which these three elements are the same are *always*
equivalent and may *always* be replaced by one another, whether in equilibrium or in movement, and this whatever
be the other forces acting.

It must be shown that two concurrent forces may always be replaced by a unique resultant; and that *this
resultant remains the same*, whether the body be at rest or in motion and whatever be the
other forces applied to it.

Finally it must be shown that forces thus defined satisfy the principle of the equality of action and reaction.

Experiment it is, and experiment alone, which can teach us all that. It will suffice to cite certain common experiments, which the scholars make daily without suspecting it, and to perform before them a few experiments, simple and well chosen.

It is after having passed through all these meanders that one may represent forces by arrows, and I should even wish that in the development of the reasonings return were made from time to time from the symbol to the reality. For instance it would not be difficult to illustrate the parallelogram of forces by aid of an apparatus formed of three strings, passing over pulleys, stretched by weights and in equilibrium while pulling on the same point.

Knowing force, it is easy to define mass; this time the definition should be borrowed from dynamics; there is no way of doing otherwise, since the end to be attained is to give understanding of the distinction between mass and weight. Here again, the definition should be led up to by experiments; there is in fact a machine which seems made expressly to show what mass is, Atwood’s machine; recall also the laws of the fall of bodies, that the acceleration of gravity is the same for heavy as for light bodies, and that it varies with the latitude, etc.

Now, if you tell me that all the methods I extol have long been applied in the schools, I shall rejoice over it more than be surprised at it. I know that on the whole our mathematical teaching is good. I do not wish it overturned; that would even distress me. I only desire betterments slowly progressive. This teaching should not be subjected to brusque oscillations under the capricious blast of ephemeral fads. In such tempests its high educative value would soon founder. A good and sound logic should continue to be its basis. The definition by example is always necessary, but it should prepare the way for the logical definition, it should not replace it; it should at least make this wished for, in the cases where the true logical definition can be advantageously given only in advanced teaching.

Understand that what I have here said does not imply giving up what I have written elsewhere. I have often had occasion to criticize certain definitions I extol to-day. These criticisms hold good completely. These definitions can only be provisory. But it is by way of them that we must pass.

Can mathematics be reduced to logic without having to appeal to principles peculiar to mathematics? There is a whole school, abounding in ardor and full of faith, striving to prove it. They have their own special language, which is without words, using only signs. This language is understood only by the initiates, so that commoners are disposed to bow to the trenchant affirmations of the adepts. It is perhaps not unprofitable to examine these affirmations somewhat closely, to see if they justify the peremptory tone with which they are presented.

But to make clear the nature of the question it is necessary to enter upon certain historical details and in particular to recall the character of the works of Cantor.

Since long ago the notion of infinity had been introduced into mathematics; but this infinite was what philosophers
call a *becoming*. The mathematical infinite was only a quantity capable of increasing beyond all limit: it was
a variable quantity of which it could not be said that it *had passed* all limits, but only that it *could
pass* them.

Cantor has undertaken to introduce into mathematics an *actual infinite*, that is to say a quantity which not
only is capable of passing all limits, but which is regarded as having already passed them. He has set himself
questions like these: Are there more points in space than whole numbers? Are there more points in space than points in
a plane? etc.

And then the number of whole numbers, that of the points of space, etc., constitutes what he calls a *transfinite
cardinal number*, that is to say a cardinal number greater than all the ordinary cardinal numbers. And he has
occupied himself in comparing these transfinite cardinal numbers. In arranging in a proper order the elements of an
aggregate containing an infinity of them, he has also imagined what he calls transfinite
ordinal numbers upon which I shall not dwell.

Many mathematicians followed his lead and set a series of questions of the sort. They so familiarized themselves with transfinite numbers that they have come to make the theory of finite numbers depend upon that of Cantor’s cardinal numbers. In their eyes, to teach arithmetic in a way truly logical, one should begin by establishing the general properties of transfinite cardinal numbers, then distinguish among them a very small class, that of the ordinary whole numbers. Thanks to this détour, one might succeed in proving all the propositions relative to this little class (that is to say all our arithmetic and our algebra) without using any principle foreign to logic. This method is evidently contrary to all sane psychology; it is certainly not in this way that the human mind proceeded in constructing mathematics; so its authors do not dream, I think, of introducing it into secondary teaching. But is it at least logic, or, better, is it correct? It may be doubted.

The geometers who have employed it are however very numerous. They have accumulated formulas and they have thought to free themselves from what was not pure logic by writing memoirs where the formulas no longer alternate with explanatory discourse as in the books of ordinary mathematics, but where this discourse has completely disappeared.

Unfortunately they have reached contradictory results, what are called the *cantorian antinomies*, to which
we shall have occasion to return. These contradictions have not discouraged them and they have tried to modify their
rules so as to make those disappear which had already shown themselves, without being sure, for all that, that new ones
would not manifest themselves.

It is time to administer justice on these exaggerations. I do not hope to convince them; for they have lived too long in this atmosphere. Besides, when one of their demonstrations has been refuted, we are sure to see it resurrected with insignificant alterations, and some of them have already risen several times from their ashes. Such long ago was the Lernæan hydra with its famous heads which always grew again. Hercules got through, since his hydra had only nine heads, or eleven; but here there are too many, some in England, some in Germany, in Italy, in France, and he would have to give up the struggle. So I appeal only to men of good judgment unprejudiced.

In these latter years numerous works have been published on pure mathematics and the philosophy of mathematics,
trying to separate and isolate the logical elements of mathematical reasoning. These works have been analyzed and
expounded very clearly by M. Couturat in a book entitled: *The Principles of Mathematics*.

For M. Couturat, the new works, and in particular those of Russell and Peano, have finally settled the controversy, so long pending between Leibnitz and Kant. They have shown that there are no synthetic judgments a priori (Kant’s phrase to designate judgments which can neither be demonstrated analytically, nor reduced to identities, nor established experimentally), they have shown that mathematics is entirely reducible to logic and that intuition here plays no rôle.

This is what M. Couturat has set forth in the work just cited; this he says still more explicitly in his Kant
jubilee discourse, so that I heard my neighbor whisper: “I well see this is the centenary of Kant’s
*death*.”

Can we subscribe to this conclusive condemnation? I think not, and I shall try to show why.

What strikes us first in the new mathematics is its purely formal character: “We think,” says Hilbert, “three sorts
of *things*, which we shall call points, straights and planes. We convene that a straight shall be determined by
two points, and that in place of saying this straight is determined by these two points, we may say it passes through
these two points, or that these two points are situated on this straight.” What these *things* are, not only we
do not know, but we should not seek to know. We have no need to, and one who never had seen either point or straight or
plane could geometrize as well as we. That the phrase *to pass through*, or the phrase
*to be situated upon* may arouse in us no image, the first is simply a synonym of to *be determined* and
the second of *to determine*.

Thus, be it understood, to demonstrate a theorem, it is neither necessary nor even advantageous to know what it
means. The geometer might be replaced by the *logic piano* imagined by Stanley Jevons; or, if you choose, a
machine might be imagined where the assumptions were put in at one end, while the theorems came out at the other, like
the legendary Chicago machine where the pigs go in alive and come out transformed into hams and sausages. No more than
these machines need the mathematician know what he does.

I do not make this formal character of his geometry a reproach to Hilbert. This is the way he should go, given the problem he set himself. He wished to reduce to a minimum the number of the fundamental assumptions of geometry and completely enumerate them; now, in reasonings where our mind remains active, in those where intuition still plays a part, in living reasonings, so to speak, it is difficult not to introduce an assumption or a postulate which passes unperceived. It is therefore only after having carried back all the geometric reasonings to a form purely mechanical that he could be sure of having accomplished his design and finished his work.

What Hilbert did for geometry, others have tried to do for arithmetic and analysis. Even if they had entirely succeeded, would the Kantians be finally condemned to silence? Perhaps not, for in reducing mathematical thought to an empty form, it is certainly mutilated.

Even admitting it were established that all the theorems could be deduced by procedures purely analytic, by simple logical combinations of a finite number of assumptions, and that these assumptions are only conventions; the philosopher would still have the right to investigate the origins of these conventions, to see why they have been judged preferable to the contrary conventions.

And then the logical correctness of the reasonings leading from the assumptions to the theorems is not the only thing which should occupy us. The rules of perfect logic, are they the whole of mathematics? As well say the whole art of playing chess reduces to the rules of the moves of the pieces. Among all the constructs which can be built up of the materials furnished by logic, choice must be made; the true geometer makes this choice judiciously because he is guided by a sure instinct, or by some vague consciousness of I know not what more profound and more hidden geometry, which alone gives value to the edifice constructed.

To seek the origin of this instinct, to study the laws of this deep geometry, felt, not stated, would also be a fine employment for the philosophers who do not want logic to be all. But it is not at this point of view I wish to put myself, it is not thus I wish to consider the question. The instinct mentioned is necessary for the inventor, but it would seem at first we might do without it in studying the science once created. Well, what I wish to investigate is if it be true that, the principles of logic once admitted, one can, I do not say discover, but demonstrate, all the mathematical verities without making a new appeal to intuition.

I once said no to this question:^{12} should our reply be modified by the
recent works? My saying no was because “the principle of complete induction” seemed to me at once necessary to the
mathematician and irreducible to logic. The statement of this principle is: “If a property be true of the number 1, and
if we establish that it is true of *n* + 1 provided it be of *n*, it will be true of all the whole
numbers.” Therein I see the mathematical reasoning par excellence. I did not mean to say, as has been supposed, that
all mathematical reasonings can be reduced to an application of this principle. Examining these reasonings closely, we
there should see applied many other analogous principles, presenting the same essential characteristics. In this
category of principles, that of complete induction is only the simplest of all and this is why I have chosen it as
type.

The current name, principle of complete induction, is not justified. This mode of reasoning is none the less a true mathematical induction which differs from ordinary induction only by its certitude.

^{12} See *Science and Hypothesis*, chapter I.

Definitions and Assumptions

The existence of such principles is a difficulty for the uncompromising logicians; how do they pretend to get out of
it? The principle of complete induction, they say, is not an assumption properly so called or a synthetic judgment
*a priori*; it is just simply the definition of whole number. It is therefore a simple convention. To discuss
this way of looking at it, we must examine a little closely the relations between definitions and assumptions.

Let us go back first to an article by M. Couturat on mathematical definitions which appeared in *l’Enseignement
mathématique*, a magazine published by Gauthier-Villars and by Georg at Geneva. We shall see there a distinction
between the *direct definition and the definition by postulates*.

“The definition by postulates,” says M. Couturat, “applies not to a single notion, but to a system of notions; it consists in enumerating the fundamental relations which unite them and which enable us to demonstrate all their other properties; these relations are postulates.”

If previously have been defined all these notions but one, then this last will be by definition the thing which verifies these postulates. Thus certain indemonstrable assumptions of mathematics would be only disguised definitions. This point of view is often legitimate; and I have myself admitted it in regard for instance to Euclid’s postulate.

The other assumptions of geometry do not suffice to completely define distance; the distance then will be, by definition, among all the magnitudes which satisfy these other assumptions, that which is such as to make Euclid’s postulate true.

Well the logicians suppose true for the principle of complete induction what I admit for Euclid’s postulate; they want to see in it only a disguised definition.

But to give them this right, two conditions must be fulfilled. Stuart Mill says every definition implies an assumption, that by which the existence of the defined object is affirmed. According to that, it would no longer be the assumption which might be a disguised definition, it would on the contrary be the definition which would be a disguised assumption. Stuart Mill meant the word existence in a material and empirical sense; he meant to say that in defining the circle we affirm there are round things in nature.

Under this form, his opinion is inadmissible. Mathematics is independent of the existence of material objects; in mathematics the word exist can have only one meaning, it means free from contradiction. Thus rectified, Stuart Mill’s thought becomes exact; in defining a thing, we affirm that the definition implies no contradiction.

If therefore we have a system of postulates, and if we can demonstrate that these postulates imply no contradiction, we shall have the right to consider them as representing the definition of one of the notions entering therein. If we can not demonstrate that, it must be admitted without proof, and that then will be an assumption; so that, seeking the definition under the postulate, we should find the assumption under the definition.

Usually, to show that a definition implies no contradiction, we proceed by *example*, we try to make an
example of a thing satisfying the definition. Take the case of a definition by postulates; we wish to define a notion
*A*, and we say that, by definition, an *A* is anything for which certain postulates are true. If we can
prove directly that all these postulates are true of a certain object *B*, the definition will be justified; the
object *B* will be an *example* of an *A*. We shall be certain that the postulates are not
contradictory, since there are cases where they are all true at the same time.

But such a direct demonstration by example is not always possible.

To establish that the postulates imply no contradiction, it is then necessary to consider all the propositions deducible from these postulates considered as premises, and to show that, among these propositions, no two are contradictory. If these propositions are finite in number, a direct verification is possible. This case is infrequent and uninteresting. If these propositions are infinite in number, this direct verification can no longer be made; recourse must be had to procedures where in general it is necessary to invoke just this principle of complete induction which is precisely the thing to be proved.

This is an explanation of one of the conditions the logicians should satisfy, *and further on we shall see they
have not done it*.

There is a second. When we give a definition, it is to use it.

We therefore shall find in the sequel of the exposition the word defined; have we the right to affirm, of the thing represented by this word, the postulate which has served for definition? Yes, evidently, if the word has retained its meaning, if we do not attribute to it implicitly a different meaning. Now this is what sometimes happens and it is usually difficult to perceive it; it is needful to see how this word comes into our discourse, and if the gate by which it has entered does not imply in reality a definition other than that stated.

This difficulty presents itself in all the applications of mathematics. The mathematical notion has been given a definition very refined and very rigorous; and for the pure mathematician all doubt has disappeared; but if one wishes to apply it to the physical sciences for instance, it is no longer a question of this pure notion, but of a concrete object which is often only a rough image of it. To say that this object satisfies, at least approximately, the definition, is to state a new truth, which experience alone can put beyond doubt, and which no longer has the character of a conventional postulate.

But without going beyond pure mathematics, we also meet the same difficulty.

You give a subtile definition of numbers; then, once this definition given, you think no more of it; because, in reality, it is not it which has taught you what number is; you long ago knew that, and when the word number further on is found under your pen, you give it the same sense as the first comer. To know what is this meaning and whether it is the same in this phrase or that, it is needful to see how you have been led to speak of number and to introduce this word into these two phrases. I shall not for the moment dilate upon this point, because we shall have occasion to return to it.

Thus consider a word of which we have given explicitly a definition *A*; afterwards in the discourse we make
a use of it which implicitly supposes another definition *B*. It is possible that these two definitions
designate the same thing. But that this is so is a new truth which must either be demonstrated or admitted as an
independent assumption.

*We shall see farther on that the logicians have not fulfilled the second condition any better than the
first.*

The definitions of number are very numerous and very different; I forego the enumeration even of the names of their authors. We should not be astonished that there are so many. If one among them was satisfactory, no new one would be given. If each new philosopher occupying himself with this question has thought he must invent another one, this was because he was not satisfied with those of his predecessors, and he was not satisfied with them because he thought he saw a petitio principii.

I have always felt, in reading the writings devoted to this problem, a profound feeling of discomfort; I was always expecting to run against a petitio principii, and when I did not immediately perceive it, I feared I had overlooked it.

This is because it is impossible to give a definition without using a sentence, and difficult to make a sentence without using a number word, or at least the word several, or at least a word in the plural. And then the declivity is slippery and at each instant there is risk of a fall into petitio principii.

I shall devote my attention in what follows only to those of these definitions where the petitio principii is most ably concealed.

The symbolic language created by Peano plays a very grand rôle in these new researches. It is capable of rendering some service, but I think M. Couturat attaches to it an exaggerated importance which must astonish Peano himself.

The essential element of this language is certain algebraic signs which represent the
different conjunctions: if, and, or, therefore. That these signs may be convenient is possible; but that they are
destined to revolutionize all philosophy is a different matter. It is difficult to admit that the word *if*
acquires, when written C, a virtue it had not when written if. This invention of Peano was first called
*pasigraphy*, that is to say the art of writing a treatise on mathematics without using a single word of
ordinary language. This name defined its range very exactly. Later, it was raised to a more eminent dignity by
conferring on it the title of *logistic*. This word is, it appears, employed at the Military Academy, to
designate the art of the quartermaster of cavalry, the art of marching and cantoning troops; but here no confusion need
be feared, and it is at once seen that this new name implies the design of revolutionizing logic.

We may see the new method at work in a mathematical memoir by Burali-Forti, entitled: *Una Questione sui numeri
transfiniti*, inserted in Volume XI of the *Rendiconti del circolo matematico di Palermo*.

I begin by saying this memoir is very interesting, and my taking it here as example is precisely because it is the most important of all those written in the new language. Besides, the uninitiated may read it, thanks to an Italian interlinear translation.

What constitutes the importance of this memoir is that it has given the first example of those antinomies met in the
study of transfinite numbers and making since some years the despair of mathematicians. The aim, says Burali-Forti, of
this note is to show there may be two transfinite numbers (ordinals), *a* and *b*, such that *a*
is neither equal to, greater than, nor less than *b*.

To reassure the reader, to comprehend the considerations which follow, he has no need of knowing what a transfinite ordinal number is.

Now, Cantor had precisely proved that between two transfinite numbers as between two finite, there can be no other relation than equality or inequality in one sense or the other. But it is not of the substance of this memoir that I wish to speak here; that would carry me much too far from my subject; I only wish to consider the form, and just to ask if this form makes it gain much in rigor and whether it thus compensates for the efforts it imposes upon the writer and the reader.

First we see Burali-Forti define the number 1 as follows:

a definition eminently fitted to give an idea of the number 1 to persons who had never heard speak of it.

I understand Peanian too ill to dare risk a critique, but still I fear this definition contains a petitio principii, considering that I see the figure 1 in the first member and Un in letters in the second.

However that may be, Burali-Forti starts from this definition and, after a short calculation, reaches the equation:

which tells us that One is a number.

And since we are on these definitions of the first numbers, we recall that M. Couturat has also defined 0 and 1.

What is zero? It is the number of elements of the null class. And what is the null class? It is that containing no element.

To define zero by null, and null by no, is really to abuse the wealth of language; so M. Couturat has introduced an improvement in his definition, by writing:

which means: zero is the number of things satisfying a condition never satisfied.

But as never means *in no case* I do not see that the progress is great.

I hasten to add that the definition M. Couturat gives of the number 1 is more satisfactory.

One, says he in substance, is the number of elements in a class in which any two elements are identical.

It is more satisfactory, I have said, in this sense that to define 1, he does not use the word one; in compensation, he uses the word two. But I fear, if asked what is two, M. Couturat would have to use the word one.

But to return to the memoir of Burali-Forti; I have said his conclusions are in direct opposition to those of Cantor. Now, one day M. Hadamard came to see me and the talk fell upon this antinomy.

“Burali-Forti’s reasoning,” I said, “does it not seem to you irreproachable?” “No, and on the contrary I find
nothing to object to in that of Cantor. Besides, Burali-Forti had no right to speak of the aggregate of *all*
the ordinal numbers.”

“Pardon, he had the right, since he could always put

I should like to know who was to prevent him, and can it be said a thing does not exist, when we have called it Ω?”

It was in vain, I could not convince him (which besides would have been sad, since he was right). Was it merely because I do not speak the Peanian with enough eloquence? Perhaps; but between ourselves I do not think so.

Thus, despite all this pasigraphic apparatus, the question was not solved. What does that prove? In so far as it is a question only of proving one a number, pasigraphy suffices, but if a difficulty presents itself, if there is an antinomy to solve, pasigraphy becomes impotent.

To justify its pretensions, logic had to change. We have seen new logics arise of which the most interesting is that of Russell. It seems he has nothing new to write about formal logic, as if Aristotle there had touched bottom. But the domain Russell attributes to logic is infinitely more extended than that of the classic logic, and he has put forth on the subject views which are original and at times well warranted.

First, Russell subordinates the logic of classes to that of propositions, while the logic of Aristotle was above all
the logic of classes and took as its point of departure the relation of subject to predicate. The classic syllogism,
“Socrates is a man,” etc., gives place to the hypothetical syllogism: “If *A* is true, *B* is true; now
if *B* is true, *C* is true,” etc. And this is, I think, a most happy idea, because the classic syllogism
is easy to carry back to the hypothetical syllogism, while the inverse transformation is not without difficulty.

And then this is not all. Russell’s logic of propositions is the study of the laws of combination of the
conjunctions *if*, *and*, *or*, and the negation *not*.

In adding here two other conjunctions, *and* and *or*, Russell opens to logic a new field. The symbols
*and*, *or* follow the same laws as the two signs × and +, that is to say the commutative associative and
distributive laws. Thus *and* represents logical multiplication, while *or* represents logical addition.
This also is very interesting.

Russell reaches the conclusion that any false proposition implies all other propositions true or false. M. Couturat says this conclusion will at first seem paradoxical. It is sufficient however to have corrected a bad thesis in mathematics to recognize how right Russell is. The candidate often is at great pains to get the first false equation; but that once obtained, it is only sport then for him to accumulate the most surprising results, some of which even may be true.

We see how much richer the new logic is than the classic logic; the symbols are multiplied and allow of varied
combinations *which are no longer limited in number*. Has one the right to give this extension to the meaning of
the word *logic*? It would be useless to examine this question and to seek with Russell a mere quarrel about
words. Grant him what he demands; but be not astonished if certain verities declared irreducible to logic in the old
sense of the word find themselves now reducible to logic in the new sense — something very different.

A great number of new notions have been introduced, and these are not simply combinations of the old. Russell knows this, and not only at the beginning of the first chapter, ‘The Logic of Propositions,’ but at the beginning of the second and third, ‘The Logic of Classes’ and ‘The Logic of Relations,’ he introduces new words that he declares indefinable.

And this is not all; he likewise introduces principles he declares indemonstrable. But these indemonstrable
principles are appeals to intuition, synthetic judgments *a priori*. We regard them as intuitive when we meet
them more or less explicitly enunciated in mathematical treatises; have they changed character because the meaning of
the word logic has been enlarged and we now find them in a book entitled *Treatise on Logic*? *They have not
changed nature; they have only changed place.*

Could these principles be considered as disguised definitions? It would then be necessary to have some way of proving that they imply no contradiction. It would be necessary to establish that, however far one followed the series of deductions, he would never be exposed to contradicting himself.

We might attempt to reason as follows: We can verify that the operations of the new logic
applied to premises exempt from contradiction can only give consequences equally exempt from contradiction. If
therefore after *n* operations we have not met contradiction, we shall not encounter it after *n* + 1.
Thus it is impossible that there should be a moment when contradiction *begins*, which shows we shall never meet
it. Have we the right to reason in this way? No, for this would be to make use of complete induction; and *remember,
we do not yet know the principle of complete induction*.

We therefore have not the right to regard these assumptions as disguised definitions and only one resource remains for us, to admit a new act of intuition for each of them. Moreover I believe this is indeed the thought of Russell and M. Couturat.

Thus each of the nine indefinable notions and of the twenty indemonstrable propositions (I believe if it were I that
did the counting, I should have found some more) which are the foundation of the new logic, logic in the broad sense,
presupposes a new and independent act of our intuition and (why not say it?) a veritable synthetic judgment *a
priori*. On this point all seem agreed, but what Russell claims, and *what seems to me doubtful, is that after
these appeals to intuition, that will be the end of it; we need make no others and can build all mathematics without
the intervention of any new element*.

M. Couturat often repeats that this new logic is altogether independent of the idea of number. I shall not amuse myself by counting how many numeral adjectives his exposition contains, both cardinal and ordinal, or indefinite adjectives such as several. We may cite, however, some examples:

“The logical product of *two* or *more* propositions is. . . . ”;

“All propositions are capable only of *two* values, true and false”;

“The relative product of *two* relations is a relation”;

“A relation exists between two terms,” etc., etc.

Sometimes this inconvenience would not be unavoidable, but sometimes also it is essential. A relation is incomprehensible without two terms; it is impossible to have the intuition of the relation, without having at the same time that of its two terms, and without noticing they are two, because, if the relation is to be conceivable, it is necessary that there be two and only two.

I reach what M. Couturat calls the *ordinal theory* which is the foundation of arithmetic properly so called.
M. Couturat begins by stating Peano’s five assumptions, which are independent, as has been proved by Peano and
Padoa.

1. Zero is an integer.

2. Zero is not the successor of any integer.

3. The successor of an integer is an integer.

To this it would be proper to add,

Every integer has a successor.

4. Two integers are equal if their successors are.

The fifth assumption is the principle of complete induction.

M. Couturat considers these assumptions as disguised definitions; they constitute the definition by postulates of zero, of successor, and of integer.

But we have seen that for a definition by postulates to be acceptable we must be able to prove that it implies no contradiction.

Is this the case here? Not at all.

The demonstration can not be made *by example*. We can not take a part of the integers, for instance the
first three, and prove they satisfy the definition.

If I take the series 0, 1, 2, I see it fulfils the assumptions 1, 2, 4 and 5; but to satisfy assumption 3 it still is necessary that 3 be an integer, and consequently that the series 0, 1, 2, 3, fulfil the assumptions; we might prove that it satisfies assumptions 1, 2, 4, 5, but assumption 3 requires besides that 4 be an integer and that the series 0, 1, 2, 3, 4 fulfil the assumptions, and so on.

It is therefore impossible to demonstrate the assumptions for certain integers without proving them for all; we must give up proof by example.

It is necessary then to take all the consequences of our assumptions and see if they contain no contradiction.

If these consequences were finite in number, this would be easy; but they are infinite in number; they are the whole of mathematics, or at least all arithmetic.

What then is to be done? Perhaps strictly we could repeat the reasoning of number III.

But as we have said, this reasoning is complete induction, and it is precisely the principle of complete induction whose justification would be the point in question.

I come now to the capital work of Hilbert which he communicated to the Congress of Mathematicians at Heidelberg, and
of which a French translation by M. Pierre Boutroux appeared in *l’Enseignement mathématique*, while an English
translation due to Halsted appeared in *The Monist*.^{13} In this work,
which contains profound thoughts, the author’s aim is analogous to that of Russell, but on many points he diverges from
his predecessor.

“But,” he says (*Monist*, p. 340), “on attentive consideration we become aware that in the usual exposition
of the laws of logic certain fundamental concepts of arithmetic are already employed; for example, the concept of the
aggregate, in part also the concept of number.

“We fall thus into a vicious circle and therefore to avoid paradoxes a partly simultaneous development of the laws of logic and arithmetic is requisite.”

We have seen above that what Hilbert says of the principles of logic *in the usual exposition* applies
likewise to the logic of Russell. So for Russell logic is prior to arithmetic; for Hilbert they are ‘simultaneous.’ We
shall find further on other differences still greater, but we shall point them out as we come to them. I prefer to
follow step by step the development of Hilbert’s thought, quoting textually the most important passages.

“Let us take as the basis of our consideration first of all a thought-thing 1 (one)” (p. 341). Notice that in so doing we in no wise imply the notion of number, because it is understood that 1 is here only a symbol and that we do not at all seek to know its meaning. “The taking of this thing together with itself respectively two, three or more times. . . . ” Ah! this time it is no longer the same; if we introduce the words ‘two,’ ‘three,’ and above all ‘more,’ ‘several,’ we introduce the notion of number; and then the definition of finite whole number which we shall presently find, will come too late. Our author was too circumspect not to perceive this begging of the question. So at the end of his work he tries to proceed to a truly patching-up process.

Hilbert then introduces two simple objects 1 and =, and considers all the combinations of these two objects, all the combinations of their combinations, etc. It goes without saying that we must forget the ordinary meaning of these two signs and not attribute any to them.

Afterwards he separates these combinations into two classes, the class of the existent and the class of the non-existent, and till further orders this separation is entirely arbitrary. Every affirmative statement tells us that a certain combination belongs to the class of the existent; every negative statement tells us that a certain combination belongs to the class of the non-existent.

^{13} ‘The Foundations of Logic and Arithmetic,’ *Monist*, XV.,
338-352.

Note now a difference of the highest importance. For Russell any object whatsoever, which he designates by
*x*, is an object absolutely undetermined and about which he supposes nothing; for Hilbert it is one of the
combinations formed with the symbols 1 and =; he could not conceive of the introduction of anything other than
combinations of objects already defined. Moreover Hilbert formulates his thought in the neatest way, and I think I must
reproduce *in extenso* his statement (p. 348):

“In the assumptions the arbitraries (as equivalent for the concept ‘every’ and ‘all’ in the customary logic) represent only those thought-things and their combinations with one another, which at this stage are laid down as fundamental or are to be newly defined. Therefore in the deduction of inferences from the assumptions, the arbitraries, which occur in the assumptions, can be replaced only by such thought-things and their combinations.

“Also we must duly remember, that through the super-addition and making fundamental of a new thought-thing the preceding assumptions undergo an enlargement of their validity, and where necessary, are to be subjected to a change in conformity with the sense.”

The contrast with Russell’s view-point is complete. For this philosopher we may substitute for *x* not only
objects already known, but anything.

Russell is faithful to his point of view, which is that of comprehension. He starts from the general idea of being, and enriches it more and more while restricting it, by adding new qualities. Hilbert on the contrary recognizes as possible beings only combinations of objects already known; so that (looking at only one side of his thought) we might say he takes the view-point of extension.

Let us continue with the exposition of Hilbert’s ideas. He introduces two assumptions which he states in his symbolic language but which signify, in the language of the uninitiated, that every quality is equal to itself and that every operation performed upon two identical quantities gives identical results.

So stated, they are evident, but thus to present them would be to misrepresent Hilbert’s thought. For him mathematics has to combine only pure symbols, and a true mathematician should reason upon them without preconceptions as to their meaning. So his assumptions are not for him what they are for the common people.

He considers them as representing the definition by postulates of the symbol (=) heretofore void of all signification. But to justify this definition we must show that these two assumptions lead to no contradiction. For this Hilbert used the reasoning of our number III, without appearing to perceive that he is using complete induction.

The end of Hilbert’s memoir is altogether enigmatic and I shall not lay stress upon it. Contradictions accumulate;
we feel that the author is dimly conscious of the *petitio principii* he has committed, and that he seeks vainly
to patch up the holes in his argument.

What does this mean? At the point of proving that the definition of the whole number by the assumption of complete induction implies no contradiction, Hilbert withdraws as Russell and Couturat withdrew, because the difficulty is too great.

Geometry, says M. Couturat, is a vast body of doctrine wherein the principle of complete induction does not enter.
That is true in a certain measure; we can not say it is entirely absent, but it enters very slightly. If we refer to
the *Rational Geometry* of Dr. Halsted (New York, John Wiley and Sons, 1904) built up in accordance with the
principles of Hilbert, we see the principle of induction enter for the first time on page 114 (unless I have made an
oversight, which is quite possible).^{14}

So geometry, which only a few years ago seemed the domain where the reign of intuition was uncontested, is to-day the realm where the logicians seem to triumph. Nothing could better measure the importance of the geometric works of Hilbert and the profound impress they have left on our conceptions.

But be not deceived. What is after all the fundamental theorem of geometry? It is that the assumptions of geometry imply no contradiction, and this we can not prove without the principle of induction.

How does Hilbert demonstrate this essential point? By leaning upon analysis and through it upon arithmetic and through it upon the principle of induction.

And if ever one invents another demonstration, it will still be necessary to lean upon this principle, since the possible consequences of the assumptions, of which it is necessary to show that they are not contradictory, are infinite in number.

^{14} Second ed., 1907, p. 86; French ed., 1911, p. 97. G. B. H.

Our conclusion straightway is that the principle of induction can not be regarded as the disguised definition of the entire world.

Here are three truths: (1) The principle of complete induction; (2) Euclid’s postulate; (3) the physical law according to which phosphorus melts at 44° (cited by M. Le Roy).

These are said to be three disguised definitions: the first, that of the whole number; the second, that of the straight line; the third, that of phosphorus.

I grant it for the second; I do not admit it for the other two. I must explain the reason for this apparent inconsistency.

First, we have seen that a definition is acceptable only on condition that it implies no contradiction. We have shown likewise that for the first definition this demonstration is impossible; on the other hand, we have just recalled that for the second Hilbert has given a complete proof.

As to the third, evidently it implies no contradiction. Does this mean that the definition guarantees, as it should, the existence of the object defined? We are here no longer in the mathematical sciences, but in the physical, and the word existence has no longer the same meaning. It no longer signifies absence of contradiction; it means objective existence.

You already see a first reason for the distinction I made between the three cases; there is a second. In the applications we have to make of these three concepts, do they present themselves to us as defined by these three postulates?

The possible applications of the principle of induction are innumerable; take, for example, one of those we have
expounded above, and where it is sought to prove that an aggregate of assumptions can lead to no contradiction. For
this we consider one of the series of syllogisms we may go on with in starting from these assumptions as premises. When
we have finished the *n*th syllogism, we see we can make still another and this is the *n* + 1th. Thus
the number *n* serves to count a series of successive operations; it is a number obtainable by successive
additions. This therefore is a number from which we may go back to unity by *successive
subtractions*. Evidently we could not do this if we had *n* = *n* − 1, since then by subtraction we
should always obtain again the same number. So the way we have been led to consider this number *n* implies a
definition of the finite whole number and this definition is the following: A finite whole number is that which can be
obtained by successive additions; it is such that *n* is not equal to *n* − 1.

That granted, what do we do? We show that if there has been no contradiction up to the *n*th syllogism, no
more will there be up to the *n* + 1th, and we conclude there never will be. You say: I have the right to draw
this conclusion, since the whole numbers are by definition those for which a like reasoning is legitimate. But that
implies another definition of the whole number, which is as follows: A whole number is that on which we may reason by
recurrence. In the particular case it is that of which we may say that, if the absence of contradiction up to the time
of a syllogism of which the number is an integer carries with it the absence of contradiction up to the time of the
syllogism whose number is the following integer, we need fear no contradiction for any of the syllogisms whose number
is an integer.

The two definitions are not identical; they are doubtless equivalent, but only in virtue of a synthetic judgment
*a priori*; we can not pass from one to the other by a purely logical procedure. Consequently we have no right
to adopt the second, after having introduced the whole number by a way that presupposes the first.

On the other hand, what happens with regard to the straight line? I have already explained this so often that I hesitate to repeat it again, and shall confine myself to a brief recapitulation of my thought. We have not, as in the preceding case, two equivalent definitions logically irreducible one to the other. We have only one expressible in words. Will it be said there is another which we feel without being able to word it, since we have the intuition of the straight line or since we represent to ourselves the straight line? First of all, we can not represent it to ourselves in geometric space, but only in representative space, and then we can represent to ourselves just as well the objects which possess the other properties of the straight line, save that of satisfying Euclid’s postulate. These objects are ‘the non-Euclidean straights,’ which from a certain point of view are not entities void of sense, but circles (true circles of true space) orthogonal to a certain sphere. If, among these objects equally capable of representation, it is the first (the Euclidean straights) which we call straights, and not the latter (the non-Euclidean straights), this is properly by definition.

And arriving finally at the third example, the definition of phosphorus, we see the true definition would be: Phosphorus is the bit of matter I see in yonder flask.

And since I am on this subject, still another word. Of the phosphorus example I said: “This proposition is a real verifiable physical law, because it means that all bodies having all the other properties of phosphorus, save its point of fusion, melt like it at 44°.” And it was answered: “No, this law is not verifiable, because if it were shown that two bodies resembling phosphorus melt one at 44° and the other at 50°, it might always be said that doubtless, besides the point of fusion, there is some other unknown property by which they differ.”

That was not quite what I meant to say. I should have written, “All bodies possessing such and such properties finite in number (to wit, the properties of phosphorus stated in the books on chemistry, the fusion-point excepted) melt at 44°.”

And the better to make evident the difference between the case of the straight and that of phosphorus, one more remark. The straight has in nature many images more or less imperfect, of which the chief are the light rays and the rotation axis of the solid. Suppose we find the ray of light does not satisfy Euclid’s postulate (for example by showing that a star has a negative parallax), what shall we do? Shall we conclude that the straight being by definition the trajectory of light does not satisfy the postulate, or, on the other hand, that the straight by definition satisfying the postulate, the ray of light is not straight?

Assuredly we are free to adopt the one or the other definition and consequently the one or the other conclusion; but to adopt the first would be stupid, because the ray of light probably satisfies only imperfectly not merely Euclid’s postulate, but the other properties of the straight line, so that if it deviates from the Euclidean straight, it deviates no less from the rotation axis of solids which is another imperfect image of the straight line; while finally it is doubtless subject to change, so that such a line which yesterday was straight will cease to be straight to-morrow if some physical circumstance has changed.

Suppose now we find that phosphorus does not melt at 44°, but at 43.9°. Shall we conclude that phosphorus being by definition that which melts at 44°, this body that we did call phosphorus is not true phosphorus, or, on the other hand, that phosphorous melts at 43.9°? Here again we are free to adopt the one or the other definition and consequently the one or the other conclusion; but to adopt the first would be stupid because we can not be changing the name of a substance every time we determine a new decimal of its fusion-point.

To sum up, Russell and Hilbert have each made a vigorous effort; they have each written a work full of original views, profound and often well warranted. These two works give us much to think about and we have much to learn from them. Among their results, some, many even, are solid and destined to live.

But to say that they have finally settled the debate between Kant and Leibnitz and ruined the Kantian theory of mathematics is evidently incorrect. I do not know whether they really believed they had done it, but if they believed so, they deceived themselves.

The logicians have attempted to answer the preceding considerations. For that, a transformation of logistic was necessary, and Russell in particular has modified on certain points his original views. Without entering into the details of the debate, I should like to return to the two questions to my mind most important: Have the rules of logistic demonstrated their fruitfulness and infallibility? Is it true they afford means of proving the principle of complete induction without any appeal to intuition?

On the question of fertility, it seems M. Couturat has naïve illusions. Logistic, according to him, lends invention
‘stilts and wings,’ and on the next page: ”*Ten years ago*, Peano published the first edition of his
*Formulaire*.” How is that, ten years of wings and not to have flown!

I have the highest esteem for Peano, who has done very pretty things (for instance his ‘space-filling curve,’ a phrase now discarded); but after all he has not gone further nor higher nor quicker than the majority of wingless mathematicians, and would have done just as well with his legs.

On the contrary I see in logistic only shackles for the inventor. It is no aid to conciseness — far from it, and if
twenty-seven equations were necessary to establish that 1 is a number, how many would be needed to prove a real
theorem? If we distinguish, with Whitehead, the individual *x*, the class of which the only member is *x*
and which shall be called ι*x*, then the class of which the only member is the class of which the only member is
*x* and which shall be called μ*x*, do you think these distinctions, useful as they may be, go far to
quicken our pace?

Logistic forces us to say all that is ordinarily left to be understood; it makes us advance step by step; this is perhaps surer but not quicker.

It is not wings you logisticians give us, but leading-strings. And then we have the right to require that these leading-strings prevent our falling. This will be their only excuse. When a bond does not bear much interest, it should at least be an investment for a father of a family.

Should your rules be followed blindly? Yes, else only intuition could enable us to distinguish among them; but then they must be infallible; for only in an infallible authority can one have a blind confidence. This, therefore, is for you a necessity. Infallible you shall be, or not at all.

You have no right to say to us: “It is true we make mistakes, but so do you.” For us to blunder is a misfortune, a very great misfortune; for you it is death.

Nor may you ask: Does the infallibility of arithmetic prevent errors in addition? The rules of calculation are
infallible, and yet we see those blunder *who do not apply these rules*; but in checking their calculation it is
at once seen where they went wrong. Here it is not at all the case; the logicians *have applied* their rules,
and they have fallen into contradiction; and so true is this, that they are preparing to change these rules and to
“sacrifice the notion of class.” Why change them if they were infallible?

“We are not obliged,” you say, “to solve *hic et nunc* all possible problems.” Oh, we do not ask so much of
you. If, in face of a problem, you would give *no* solution, we should have nothing to say; but on the contrary
you give us *two* of them and those contradictory, and consequently at least one false; this it is which is
failure.

Russell seeks to reconcile these contradictions, which can only be done, according to him, “by restricting or even sacrificing the notion of class.” And M. Couturat, discovering the success of his attempt, adds: “If the logicians succeed where others have failed, M. Poincaré will remember this phrase, and give the honor of the solution to logistic.”

But no! Logistic exists, it has its code which has already had four editions; or rather this code is logistic itself. Is Mr. Russell preparing to show that one at least of the two contradictory reasonings has transgressed the code? Not at all; he is preparing to change these laws and to abrogate a certain number of them. If he succeeds, I shall give the honor of it to Russell’s intuition and not to the Peanian logistic which he will have destroyed.

I made two principal objections to the definition of whole number adopted in logistic. What says M. Couturat to the first of these objections?

What does the word *exist* mean in mathematics? It means, I said, to be free from contradiction. This M.
Couturat contests. “Logical existence,” says he, “is quite another thing from the absence of contradiction. It consists
in the fact that a class is not empty.” To say: *a*‘s exist, is, by definition, to affirm that the class
*a* is not null.

And doubtless to affirm that the class *a* is not null, is, by definition, to affirm that *a*‘s exist.
But one of the two affirmations is as denuded of meaning as the other, if they do not both signify, either that one may
see or touch *a*‘s which is the meaning physicists or naturalists give them, or that one may conceive an
*a* without being drawn into contradictions, which is the meaning given them by logicians and
mathematicians.

For M. Couturat, “it is not non-contradiction that proves existence, but it is existence that proves
non-contradiction.” To establish the existence of a class, it is necessary therefore to establish, by an
*example*, that there is an individual belonging to this class: “But, it will be said, how is the existence of
this individual proved? Must not this existence be established, in order that the existence of the class of which it is
a part may be deduced? Well, no; however paradoxical may appear the assertion, we never demonstrate the existence of an
individual. Individuals, just because they are individuals, are always considered as existent. . . . We never
have to express that an individual exists, absolutely speaking, but only that it exists in a class.” M. Couturat finds his own assertion paradoxical, and he will certainly not be the only one. Yet it must
have a meaning. It doubtless means that the existence of an individual, alone in the world, and of which nothing is
affirmed, can not involve contradiction; in so far as it is all alone it evidently will not embarrass any one. Well, so
let it be; we shall admit the existence of the individual, ‘absolutely speaking,’ but nothing more. It remains to prove
the existence of the individual ‘in a class,’ and for that it will always be necessary to prove that the affirmation,
“Such an individual belongs to such a class,” is neither contradictory in itself, nor to the other postulates
adopted.

“It is then,” continues M. Couturat, “arbitrary and misleading to maintain that a definition is valid only if we
first prove it is not contradictory.” One could not claim in prouder and more energetic terms the liberty of
contradiction. “In any case, the *onus probandi* rests upon those who believe that these principles are
contradictory.” Postulates are presumed to be compatible until the contrary is proved, just as the accused person is
presumed innocent. Needless to add that I do not assent to this claim. But, you say, the demonstration you require of
us is impossible, and you can not ask us to jump over the moon. Pardon me; that is impossible for you, but not for us,
who admit the principle of induction as a synthetic judgment *a priori*. And that would be necessary for you, as
for us.

To demonstrate that a system of postulates implies no contradiction, it is necessary to apply the principle of complete induction; this mode of reasoning not only has nothing ‘bizarre’ about it, but it is the only correct one. It is not ‘unlikely’ that it has ever been employed; and it is not hard to find ‘examples and precedents’ of it. I have cited two such instances borrowed from Hilbert’s article. He is not the only one to have used it, and those who have not done so have been wrong. What I have blamed Hilbert for is not his having recourse to it (a born mathematician such as he could not fail to see a demonstration was necessary and this the only one possible), but his having recourse without recognizing the reasoning by recurrence.

I pointed out a second error of logistic in Hilbert’s article. To-day Hilbert is excommunicated and M. Couturat no longer regards him as of the logistic cult; so he asks if I have found the same fault among the orthodox. No, I have not seen it in the pages I have read; I know not whether I should find it in the three hundred pages they have written which I have no desire to read.

Only, they must commit it the day they wish to make any application of mathematics. This science has not as sole object the eternal contemplation of its own navel; it has to do with nature and some day it will touch it. Then it will be necessary to shake off purely verbal definitions and to stop paying oneself with words.

To go back to the example of Hilbert: always the point at issue is reasoning by recurrence and the question of knowing whether a system of postulates is not contradictory. M. Couturat will doubtless say that then this does not touch him, but it perhaps will interest those who do not claim, as he does, the liberty of contradiction.

We wish to establish, as above, that we shall never encounter contradiction after any number of deductions whatever,
provided this number be finite. For that, it is necessary to apply the principle of induction. Should we here
understand by finite number every number to which by definition the principle of induction applies? Evidently not, else
we should be led to most embarrassing consequences. To have the right to lay down a system of postulates, we must be
sure they are not contradictory. This is a truth admitted by *most* scientists; I should have written *by
all* before reading M. Couturat’s last article. But what does this signify? Does it mean that we must be sure of
not meeting contradiction after a *finite* number of propositions, the *finite* number being by
definition that which has all properties of recurrent nature, so that if one of these properties fails — if, for
instance, we come upon a contradiction — we shall agree to say that the number in question is not finite? In other
words, do we mean that we must be sure not to meet contradictions, on condition of agreeing to
stop just when we are about to encounter one? To state such a proposition is enough to condemn it.

So, Hilbert’s reasoning not only assumes the principle of induction, but it supposes that this principle is given us
not as a simple definition, but as a synthetic judgment *a priori*.

To sum up:

A demonstration is necessary.

The only demonstration possible is the proof by recurrence.

This is legitimate only if we admit the principle of induction and if we regard it not as a definition but as a synthetic judgment.

Now to examine Russell’s new memoir. This memoir was written with the view to conquer the difficulties raised by those Cantor antinomies to which frequent allusion has already been made. Cantor thought he could construct a science of the infinite; others went on in the way he opened, but they soon ran foul of strange contradictions. These antinomies are already numerous, but the most celebrated are:

1. The Burali-Forti antinomy;

2. The Zermelo-König antinomy;

3. The Richard antinomy.

Cantor proved that the ordinal numbers (the question is of transfinite ordinal numbers, a new notion introduced by
him) can be ranged in a linear series; that is to say that of two unequal ordinals one is always less than the other.
Burali-Forti proves the contrary; and in fact he says in substance that if one could range *all* the ordinals in
a linear series, this series would define an ordinal greater than *all* the others; we could afterwards adjoin 1
and would obtain again an ordinal which would be *still greater*, and this is contradictory.

We shall return later to the Zermelo-König antinomy which is of a slightly different nature. The Richard
antinomy^{15} is as follows: Consider all the decimal numbers definable by a
finite number of words; these decimal numbers form an aggregate *E*, and it is easy to
see that this aggregate is countable, that is to say we can *number* the different decimal numbers of this
assemblage from 1 to infinity. Suppose the numbering effected, and define a number *N* as follows: If the
*n*th decimal of the *n*th number of the assemblage *E* is

0, 1, 2, 3, 4, 5, 6, 7, 8, 9

the *n*th decimal of *N* shall be:

1, 2, 3, 4, 5, 6, 7, 8, 1, 1

As we see, *N* is not equal to the *n*th number of *E*, and as *n* is
arbitrary, *N* does not appertain to *E* and yet *N* should belong to this assemblage since we
have defined it with a finite number of words.

We shall later see that M. Richard has himself given with much sagacity the explanation of his paradox and that this
extends, *mutatis mutandis*, to the other like paradoxes. Again, Russell cites another quite amusing paradox:
*What is the least whole number which can not be defined by a phrase composed of less than a hundred English
words*?

This number exists; and in fact the numbers capable of being defined by a like phrase are evidently finite in number since the words of the English language are not infinite in number. Therefore among them will be one less than all the others. And, on the other hand, this number does not exist, because its definition implies contradiction. This number, in fact, is defined by the phrase in italics which is composed of less than a hundred English words; and by definition this number should not be capable of definition by a like phrase.

^{15} *Revue générale des sciences*, June 30, 1905.

What is Mr. Russell’s attitude in presence of these contradictions? After having analyzed those of which we have just spoken, and cited still others, after having given them a form recalling Epimenides, he does not hesitate to conclude: “A propositional function of one variable does not always determine a class.” A propositional function (that is to say a definition) does not always determine a class. A ‘propositional function’ or ‘norm’ may be ‘non-predicative.’ And this does not mean that these non-predicative propositions determine an empty class, a null class; this does not mean that there is no value of x satisfying the definition and capable of being one of the elements of the class. The elements exist, but they have no right to unite in a syndicate to form a class.

But this is only the beginning and it is needful to know how to recognize whether a definition is or is not predicative. To solve this problem Russell hesitates between three theories which he calls

A. The zigzag theory;

B. The theory of limitation of size;

C. The no-class theory.

According to the zigzag theory “definitions (propositional functions) determine a class when they are very simple and cease to do so only when they are complicated and obscure.” Who, now, is to decide whether a definition may be regarded as simple enough to be acceptable? To this question there is no answer, if it be not the loyal avowal of a complete inability: “The rules which enable us to recognize whether these definitions are predicative would be extremely complicated and can not commend themselves by any plausible reason. This is a fault which might be remedied by greater ingenuity or by using distinctions not yet pointed out. But hitherto in seeking these rules, I have not been able to find any other directing principle than the absence of contradiction.”

This theory therefore remains very obscure; in this night a single light — the word zigzag. What Russell calls the ‘zigzaginess’ is doubtless the particular characteristic which distinguishes the argument of Epimenides.

According to the theory of limitation of size, a class would cease to have the right to exist if it were too extended. Perhaps it might be infinite, but it should not be too much so. But we always meet again the same difficulty; at what precise moment does it begin to be too much so? Of course this difficulty is not solved and Russell passes on to the third theory.

In the no-classes theory it is forbidden to speak the word ‘class’ and this word must be replaced by various
periphrases. What a change for logistic which talks only of classes and classes of classes! It becomes necessary to
remake the whole of logistic. Imagine how a page of logistic would look upon suppressing all the propositions where it
is a question of class. There would only be some scattered survivors in the midst of a blank page. *Apparent rari
nantes in gurgite vasto.*

Be that as it may, we see how Russell hesitates and the modifications to which he submits the fundamental principles he has hitherto adopted. Criteria are needed to decide whether a definition is too complex or too extended, and these criteria can only be justified by an appeal to intuition.

It is toward the no-classes theory that Russell finally inclines. Be that as it may, logistic is to be remade and it is not clear how much of it can be saved. Needless to add that Cantorism and logistic are alone under consideration; real mathematics, that which is good for something, may continue to develop in accordance with its own principles without bothering about the storms which rage outside it, and go on step by step with its usual conquests which are final and which it never has to abandon.

What choice ought we to make among these different theories? It seems to me that the solution is contained in a
letter of M. Richard of which I have spoken above, to be found in the *Revue générale des sciences* of June 30,
1905. After having set forth the antinomy we have called Richard’s antinomy, he gives its explanation. Recall what has
already been said of this antinomy. *E* is the aggregate of *all* the numbers definable by a finite
number of words, *without introducing the notion of the aggregate E itself*. Else the definition of *E*
would contain a vicious circle; we must not define *E* by the aggregate *E* itself.

Now we have defined *N* with a finite number of words, it is true, but with the aid
of the notion of the aggregate *E*. And this is why *N* is not part of *E*. In the example
selected by M. Richard, the conclusion presents itself with complete evidence and the evidence will appear still
stronger on consulting the text of the letter itself. But the same explanation holds good for the other antinomies, as
is easily verified. Thus *the definitions which should be regarded as not predicative are those which contain a
vicious circle*. And the preceding examples sufficiently show what I mean by that. Is it this which Russell calls
the ‘zigzaginess’? I put the question without answering it.

Let us now examine the pretended demonstrations of the principle of induction and in particular those of Whitehead and of Burali-Forti.

We shall speak of Whitehead’s first, and take advantage of certain new terms happily introduced by Russell in his
recent memoir. Call *recurrent class* every class containing zero, and containing *n* + 1 if it contains
*n*. Call *inductive number* every number which is a part of *all* the recurrent classes. Upon
what condition will this latter definition, which plays an essential rôle in Whitehead’s proof, be ‘predicative’ and
consequently acceptable?

In accordance with what has been said, it is necessary to understand by *all* the recurrent classes, all
those in whose definition the notion of inductive number does not enter. Else we fall again upon the vicious circle
which has engendered the antinomies.

Now *Whitehead has not taken this precaution*. Whitehead’s reasoning is therefore fallacious; it is the same
which led to the antinomies. It was illegitimate when it gave false results; it remains illegitimate when by chance it
leads to a true result.

A definition containing a vicious circle defines nothing. It is of no use to say, we are sure, whatever meaning we may give to our definition, zero at least belongs to the class of inductive numbers; it is not a question of knowing whether this class is void, but whether it can be rigorously deliminated. A ‘non-predicative’ class is not an empty class, it is a class whose boundary is undetermined. Needless to add that this particular objection leaves in force the general objections applicable to all the demonstrations.

Burali-Forti has given another demonstration.^{16} But he is obliged to assume
two postulates: First, there always exists at least one infinite class. The second is thus expressed:

The first postulate is not more evident than the principle to be proved. The second not only is not evident, but it is false, as Whitehead has shown; as moreover any recruit would see at the first glance, if the axiom had been stated in intelligible language, since it means that the number of combinations which can be formed with several objects is less than the number of these objects.

^{16} In his article ‘Le classi finite,’ *Atti di Torino*, Vol.
XXXII.

A famous demonstration by Zermelo rests upon the following assumption: In any aggregate (or the same in each
aggregate of an assemblage of aggregates) we can always choose *at random* an element (even if this assemblage
of aggregates should contain an infinity of aggregates). This assumption had been applied a thousand times without
being stated, but, once stated, it aroused doubts. Some mathematicians, for instance M. Borel, resolutely reject it;
others admire it. Let us see what, according to his last article, Russell thinks of it. He does not speak out, but his
reflections are very suggestive.

And first a picturesque example: Suppose we have as many pairs of shoes as there are whole numbers, and so that we
can number *the pairs* from one to infinity, how many shoes shall we have? Will the number of shoes be equal to
the number of pairs? Yes, if in each pair the right shoe is distinguishable from the left; it will in fact suffice to
give the number 2*n* − 1 to the right shoe of the *n*th pair, and the number 2*n* to the
left shoe of the *n*th pair. No, if the right shoe is just like the left, because a
similar operation would become impossible — unless we admit Zermelo’s assumption, since then we could choose *at
random* in each pair the shoe to be regarded as the right.

A demonstration truly founded upon the principles of analytic logic will be composed of a series of propositions. Some, serving as premises, will be identities or definitions; the others will be deduced from the premises step by step. But though the bond between each proposition and the following is immediately evident, it will not at first sight appear how we get from the first to the last, which we may be tempted to regard as a new truth. But if we replace successively the different expressions therein by their definition and if this operation be carried as far as possible, there will finally remain only identities, so that all will reduce to an immense tautology. Logic therefore remains sterile unless made fruitful by intuition.

This I wrote long ago; logistic professes the contrary and thinks it has proved it by actually proving new truths.
By what mechanism? Why in applying to their reasonings the procedure just described — namely, replacing the terms
defined by their definitions — do we not see them dissolve into identities like ordinary reasonings? It is because this
procedure is not applicable to them. And why? Because their definitions are not predicative and present this sort of
hidden vicious circle which I have pointed out above; non-predicative definitions can not be substituted for the terms
defined. Under these conditions *logistic is not sterile, it engenders antinomies*.

It is the belief in the existence of the actual infinite which has given birth to those non-predicative definitions.
Let me explain. In these definitions the word ‘all’ figures, as is seen in the examples cited above. The word ‘all’ has
a very precise meaning when it is a question of a finite number of objects; to have another one, when the objects are
infinite in number, would require there being an actual (given complete) infinity. Otherwise
*all* these objects could not be conceived as postulated anteriorly to their definition, and then if the
definition of a notion *N* depends upon *all* the objects *A*, it may be infected with a vicious
circle, if among the objects *A* are some indefinable without the intervention of the notion *N*
itself.

The rules of formal logic express simply the properties of all possible classifications. But for them to be
applicable it is necessary that these classifications be immutable and that we have no need to modify them in the
course of the reasoning. If we have to classify only a finite number of objects, it is easy to keep our classifications
without change. If the objects are *indefinite* in number, that is to say if one is constantly exposed to seeing
new and unforeseen objects arise, it may happen that the appearance of a new object may require the classification to
be modified, and thus it is we are exposed to antinomies. *There is no actual (given complete) infinity.* The
Cantorians have forgotten this, and they have fallen into contradiction. It is true that Cantorism has been of service,
but this was when applied to a real problem whose terms were precisely defined, and then we could advance without
fear.

Logistic also forgot it, like the Cantorians, and encountered the same difficulties. But the question is to know
whether they went this way by accident or whether it was a necessity for them. For me, the question is not doubtful;
belief in an actual infinity is essential in the Russell logic. It is just this which distinguishes it from the Hilbert
logic. Hilbert takes the view-point of extension, precisely in order to avoid the Cantorian antinomies. Russell takes
the view-point of comprehension. Consequently for him the genus is anterior to the species, and the *summum
genus* is anterior to all. That would not be inconvenient if the *summum genus* was finite; but if it is
infinite, it is necessary to postulate the infinite, that is to say to regard the infinite as actual (given complete).
And we have not only infinite classes; when we pass from the genus to the species in restricting the concept by new
conditions, these conditions are still infinite in number. Because they express generally that the envisaged object
presents such or such a relation with all the objects of an infinite class.

But that is ancient history. Russell has perceived the peril and takes counsel. He is about to change everything, and, what is easily understood, he is preparing not only to introduce new principles which shall allow of operations formerly forbidden, but he is preparing to forbid operations he formerly thought legitimate. Not content to adore what he burned, he is about to burn what he adored, which is more serious. He does not add a new wing to the building, he saps its foundation.

The old logistic is dead, so much so that already the zigzag theory and the no-classes theory are disputing over the succession. To judge of the new, we shall await its coming.

The New Mechanics

The general principles of Dynamics, which have, since Newton, served as foundation for physical science, and which appeared immovable, are they on the point of being abandoned or at least profoundly modified? This is what many people have been asking themselves for some years. According to them, the discovery of radium has overturned the scientific dogmas we believed the most solid: on the one hand, the impossibility of the transmutation of metals; on the other hand, the fundamental postulates of mechanics.

Perhaps one is too hasty in considering these novelties as finally established, and breaking our idols of yesterday; perhaps it would be proper, before taking sides, to await experiments more numerous and more convincing. None the less is it necessary, from to-day, to know the new doctrines and the arguments, already very weighty, upon which they rest.

In few words let us first recall in what those principles consist:

*A.* The motion of a material point isolated and apart from all exterior force is straight and uniform; this
is the principle of inertia: without force no acceleration;

*B.* The acceleration of a moving point has the same direction as the resultant of all the forces to which it
is subjected; it is equal to the quotient of this resultant by a coefficient called *mass* of the moving
point.

The mass of a moving point, so defined, is a constant; it does not depend upon the velocity
acquired by this point; it is the same whether the force, being parallel to this velocity, tends only to accelerate or
to retard the motion of the point, or whether, on the contrary, being perpendicular to this velocity, it tends to make
this motion deviate toward the right, or the left, that is to say to *curve* the trajectory;

*C.* All the forces affecting a material point come from the action of other material points; they depend
only upon the *relative* positions and velocities of these different material points.

Combining the two principles *B* and *C*, we reach the *principle of relative motion*, in
virtue of which the laws of the motion of a system are the same whether we refer this system to fixed axes, or to
moving axes animated by a straight and uniform motion of translation, so that it is impossible to distinguish absolute
motion from a relative motion with reference to such moving axes;

*D.* If a material point *A* acts upon another material point *B*, the body *B* reacts
upon *A*, and these two actions are two equal and directly opposite forces. This is *the principle of the
equality of action and reaction*, or, more briefly, the *principle of reaction*.

Astronomic observations and the most ordinary physical phenomena seem to have given of these principles a confirmation complete, constant and very precise. This is true, it is now said, but it is because we have never operated with any but very small velocities; Mercury, for example, the fastest of the planets, goes scarcely 100 kilometers a second. Would this planet act the same if it went a thousand times faster? We see there is yet no need to worry; whatever may be the progress of automobilism, it will be long before we must give up applying to our machines the classic principles of dynamics.

How then have we come to make actual speeds a thousand times greater than that of Mercury, equal, for instance, to a tenth or a third of the velocity of light, or approaching still more closely to that velocity? It is by aid of the cathode rays and the rays from radium.

We know that radium emits three kinds of rays, designated by the three Greek letters α, β, γ; in what follows, unless the contrary be expressly stated, it will always be a question of the β rays, which are analogous to the cathode rays.

After the discovery of the cathode rays two theories appeared. Crookes attributed the phenomena to a veritable molecular bombardment; Hertz, to special undulations of the ether. This was a renewal of the debate which divided physicists a century ago about light; Crookes took up the emission theory, abandoned for light; Hertz held to the undulatory theory. The facts seem to decide in favor of Crookes.

It has been recognized, in the first place, that the cathode rays carry with them a negative electric charge; they are deviated by a magnetic field and by an electric field; and these deviations are precisely such as these same fields would produce upon projectiles animated by a very high velocity and strongly charged with electricity. These two deviations depend upon two quantities: one the velocity, the other the relation of the electric charge of the projectile to its mass; we cannot know the absolute value of this mass, nor that of the charge, but only their relation; in fact, it is clear that if we double at the same time the charge and the mass, without changing the velocity, we shall double the force which tends to deviate the projectile, but, as its mass is also doubled, the acceleration and deviation observable will not be changed. The observation of the two deviations will give us therefore two equations to determine these two unknowns. We find a velocity of from 10,000 to 30,000 kilometers a second; as to the ratio of the charge to the mass, it is very great. We may compare it to the corresponding ratio in regard to the hydrogen ion in electrolysis; we then find that a cathodic projectile carries about a thousand times more electricity than an equal mass of hydrogen would carry in an electrolyte.

To confirm these views, we need a direct measurement of this velocity to compare with the velocity so calculated. Old experiments of J. J. Thomson had given results more than a hundred times too small; but they were exposed to certain causes of error. The question was taken up again by Wiechert in an arrangement where the Hertzian oscillations were utilized; results were found agreeing with the theory, at least as to order of magnitude; it would be of great interest to repeat these experiments. However that may be, the theory of undulations appears powerless to account for this complex of facts.

The same calculations made with reference to the β rays of radium have given velocities still greater: 100,000 or 200,000 kilometers or more yet. These velocities greatly surpass all those we know. It is true that light has long been known to go 300,000 kilometers a second; but it is not a carrying of matter, while, if we adopt the emission theory for the cathode rays, there would be material molecules really impelled at the velocities in question, and it is proper to investigate whether the ordinary laws of mechanics are still applicable to them.

We know that electric currents produce the phenomena of induction, in particular *self-induction*. When a
current increases, there develops an electromotive force of self-induction which tends to oppose the current; on the
contrary, when the current decreases, the electromotive force of self-induction tends to maintain the current. The
self-induction therefore opposes every variation of the intensity of the current, just as in mechanics the inertia of a
body opposes every variation of its velocity.

*Self-induction is a veritable inertia.* Everything happens as if the current could not establish itself
without putting in motion the surrounding ether and as if the inertia of this ether tended, in consequence, to keep
constant the intensity of this current. It would be requisite to overcome this inertia to establish the current, it
would be necessary to overcome it again to make the current cease.

A cathode ray, which is a rain of projectiles charged with negative electricity, may be likened to a current;
doubtless this current differs, at first sight at least, from the currents of ordinary conduction, where the matter
does not move and where the electricity circulates through the matter. This is a *current of convection*, where
the electricity, attached to a material vehicle, is carried along by the motion of this vehicle. But Rowland has proved
that currents of convection produce the same magnetic effects as currents of conduction; they should produce also the
same effects of induction. First, if this were not so, the principle of the conservation of energy would be violated;
besides, Crémieu and Pender have employed a method putting in evidence *directly* these
effects of induction.

If the velocity of a cathode corpuscle varies, the intensity of the corresponding current will likewise vary; and there will develop effects of self-induction which will tend to oppose this variation. These corpuscles should therefore possess a double inertia: first their own proper inertia, and then the apparent inertia, due to self-induction, which produces the same effects. They will therefore have a total apparent mass, composed of their real mass and of a fictitious mass of electromagnetic origin. Calculation shows that this fictitious mass varies with the velocity, and that the force of inertia of self-induction is not the same when the velocity of the projectile accelerates or slackens, or when it is deviated; therefore so it is with the force of the total apparent inertia.

The total apparent mass is therefore not the same when the real force applied to the corpuscle is parallel to its
velocity and tends to accelerate the motion as when it is perpendicular to this velocity and tends to make the
direction vary. It is necessary therefore to distinguish the *total longitudinal mass* from the *total
transversal mass*. These two total masses depend, moreover, upon the velocity. This follows from the theoretical
work of Abraham.

In the measurements of which we speak in the preceding section, what is it we determine in measuring the two
deviations? It is the velocity on the one hand, and on the other hand the ratio of the charge to the *total
transversal mass*. How, under these conditions, can we make out in this total mass the part of the real mass and
that of the fictitious electromagnetic mass? If we had only the cathode rays properly so called, it could not be
dreamed of; but happily we have the rays of radium which, as we have seen, are notably swifter. These rays are not all
identical and do not behave in the same way under the action of an electric field and a magnetic field. It is found
that the electric deviation is a function of the magnetic deviation, and we are able, by receiving on a sensitive plate
radium rays which have been subjected to the action of the two fields, to photograph the curve which represents the
relation between these two deviations. This is what Kaufmann has done, deducing from it the relation between the velocity and the ratio of the charge to the total apparent mass, a ratio we shall call
ε.

One might suppose there are several species of rays, each characterized by a fixed velocity, by a fixed charge and
by a fixed mass. But this hypothesis is improbable; why, in fact, would all the corpuscles of the same mass take always
the same velocity? It is more natural to suppose that the charge as well as the *real* mass are the same for all
the projectiles, and that these differ only by their velocity. If the ratio ε is a function of the velocity, this is
not because the real mass varies with this velocity; but, since the fictitious electromagnetic mass depends upon this
velocity, the total apparent mass, alone observable, must depend upon it, though the real mass does not depend upon it
and may be constant.

The calculations of Abraham let us know the law according to which the *fictitious* mass varies as a function
of the velocity; Kaufmann’s experiment lets us know the law of variation of the *total* mass.

The comparison of these two laws will enable us therefore to determine the ratio of the real mass to the total mass.

Such is the method Kaufmann used to determine this ratio. The result is highly surprising: *the real mass is
naught*.

This has led to conceptions wholly unexpected. What had only been proved for cathode corpuscles was extended to all
bodies. What we call mass would be only semblance; all inertia would be of electromagnetic origin. But then mass would
no longer be constant, it would augment with the velocity; sensibly constant for velocities up to 1,000 kilometers a
second, it then would increase and would become infinite for the velocity of light. The transversal mass would no
longer be equal to the longitudinal: they would only be nearly equal if the velocity is not too great. The principle
*B* of mechanics would no longer be true.

At the point where we now are, this conclusion might seem premature. Can one apply to all matter what has been
proved only for such light corpuscles, which are a mere emanation of matter and perhaps not
true matter? But before entering upon this question, a word must be said of another sort of rays. I refer to the
*canal rays*, the *Kanalstrahlen* of Goldstein.

The cathode, together with the cathode rays charged with negative electricity, emits canal rays charged with
positive electricity. In general, these canal rays not being repelled by the cathode, are confined to the immediate
neighborhood of this cathode, where they constitute the ‘chamois cushion,’ not very easy to perceive; but, if the
cathode is pierced with holes and if it almost completely blocks up the tube, the canal rays spread *back* of
the cathode, in the direction opposite to that of the cathode rays, and it becomes possible to study them. It is thus
that it has been possible to show their positive charge and to show that the magnetic and electric deviations still
exist, as for the cathode rays, but are much feebler.

Radium likewise emits rays analogous to the canal rays, and relatively very absorbable, called α rays.

We can, as for the cathode rays, measure the two deviations and thence deduce the velocity and the ratio ε. The
results are less constant than for the cathode rays, but the velocity is less, as well as the ratio ε; the positive
corpuscles are less charged than the negative; or if, which is more natural, we suppose the charges equal and of
opposite sign, the positive corpuscles are much the larger. These corpuscles, charged the ones positively, the others
negatively, have been called *electrons*.

But the electrons do not merely show us their existence in these rays where they are endowed with enormous velocities. We shall see them in very different rôles, and it is they that account for the principal phenomena of optics and electricity. The brilliant synthesis about to be noticed is due to Lorentz.

Matter is formed solely of electrons carrying enormous charges, and, if it seems to us neutral, this is because the charges of opposite sign of these electrons compensate each other. We may imagine, for example, a sort of solar system formed of a great positive electron, around which gravitate numerous little planets, the negative electrons, attracted by the electricity of opposite name which charges the central electron. The negative charges of these planets would balance the positive charge of this sun, so that the algebraic sum of all these charges would be naught.

All these electrons swim in the ether. The ether is everywhere identically the same, and perturbations in it are
propagated according to the same laws as light or the Hertzian oscillations *in vacuo*. There is nothing but
electrons and ether. When a luminous wave enters a part of the ether where electrons are numerous, these electrons are
put in motion under the influence of the perturbation of the ether, and they then react upon the ether. So would be
explained refraction, dispersion, double refraction and absorption. Just so, if for any cause an electron be put in
motion, it would trouble the ether around it and would give rise to luminous waves, and this would explain the emission
of light by incandescent bodies.

In certain bodies, the metals for example, we should have fixed electrons, between which would circulate moving electrons enjoying perfect liberty, save that of going out from the metallic body and breaking the surface which separates it from the exterior void or from the air, or from any other non-metallic body.

These movable electrons behave then, within the metallic body, as do, according to the kinetic theory of gases, the
molecules of a gas within the vase where this gas is confined. But, under the influence of a difference of potential,
the negative movable electrons would tend to go all to one side, and the positive movable electrons to the other. This
is what would produce electric currents, and *this is why these bodies would be conductors*. On the other hand,
the velocities of our electrons would be the greater the higher the temperature, if we accept the assimilation with the
kinetic theory of gases. When one of these movable electrons encounters the surface of the metallic body, whose
boundary it can not pass, it is reflected like a billiard ball which has hit the cushion, and its velocity undergoes a
sudden change of direction. But when an electron changes direction, as we shall see further on,
it becomes the source of a luminous wave, and this is why hot metals are incandescent.

In other bodies, the dielectrics and the transparent bodies, the movable electrons enjoy much less freedom. They remain as if attached to fixed electrons which attract them. The farther they go away from them the greater becomes this attraction and tends to pull them back. They therefore can make only small excursions; they can no longer circulate, but only oscillate about their mean position. This is why these bodies would not be conductors; moreover they would most often be transparent, and they would be refractive, since the luminous vibrations would be communicated to the movable electrons, susceptible of oscillation, and thence a perturbation would result.

I can not here give the details of the calculations; I confine myself to saying that this theory accounts for all the known facts, and has predicted new ones, such as the Zeeman effect.

We now may face two hypotheses:

1º The positive electrons have a real mass, much greater than their fictitious electromagnetic mass; the negative electrons alone lack real mass. We might even suppose that apart from electrons of the two signs, there are neutral atoms which have only their real mass. In this case, mechanics is not affected; there is no need of touching its laws; the real mass is constant; simply, motions are deranged by the effects of self-induction, as has always been known; moreover, these perturbations are almost negligible, except for the negative electrons which, not having real mass, are not true matter.

2º But there is another point of view; we may suppose there are no neutral atoms, and the positive electrons lack
real mass just as the negative electrons. But then, real mass vanishing, either the word *mass* will no longer
have any meaning, or else it must designate the fictitious electromagnetic mass; in this case, mass will no longer be
constant, the transversal *mass* will no longer be equal to the longitudinal, the principles of mechanics will
be overthrown.

First a word of explanation. We have said that, for the same charge, the *total* mass of a positive electron
is much greater than that of a negative. And then it is natural to think that this difference is explained by the
positive electron having, besides its fictitious mass, a considerable real mass; which takes us back to the first
hypothesis. But we may just as well suppose that the real mass is null for these as for the others, but that the
fictitious mass of the positive electron is much the greater since this electron is much the smaller. I say advisedly:
much the smaller. And, in fact, in this hypothesis inertia is exclusively electromagnetic in origin; it reduces itself
to the inertia of the ether; the electrons are no longer anything by themselves; they are solely holes in the ether and
around which the ether moves; the smaller these holes are, the more will there be of ether, the greater, consequently,
will be the inertia of the ether.

How shall we decide between these two hypotheses? By operating upon the canal rays as Kaufmann did upon the β rays? This is impossible; the velocity of these rays is much too slight. Should each therefore decide according to his temperament, the conservatives going to one side and the lovers of the new to the other? Perhaps, but, to fully understand the arguments of the innovators, other considerations must come in.

You know in what the phenomenon of aberration, discovered by Bradley, consists. The light issuing from a star takes
a certain time to go through a telescope; during this time, the telescope, carried along by the motion of the earth, is
displaced. If therefore the telescope were pointed in the *true* direction of the star, the image would be
formed at the point occupied by the crossing of the threads of the network when the light has reached the objective;
and this crossing would no longer be at this same point when the light reached the plane of the network. We would
therefore be led to mis-point the telescope to bring the image upon the crossing of the threads. Thence results that
the astronomer will not point the telescope in the direction of the absolute velocity of the light, that is to say
toward the true position of the star, but just in the direction of the relative velocity of the light with reference to
the earth, that is to say toward what is called the apparent position of the star.

The velocity of light is known; we might therefore suppose that we have the means of calculating the
*absolute* velocity of the earth. (I shall soon explain my use here of the word absolute.) Nothing of the sort;
we indeed know the apparent position of the star we observe; but we do not know its true position; we know the velocity
of the light only in magnitude and not in direction.

If therefore the absolute velocity of the earth were straight and uniform, we should never have suspected the
phenomenon of aberration; but it is variable; it is composed of two parts: the velocity of the solar system, which is
straight and uniform; the velocity of the earth with reference to the sun, which is variable. If the velocity of the
solar system, that is to say if the constant part existed alone, the observed direction would be invariable. This position that one would thus observe is called the *mean* apparent position of the
star.

Taking account now at the same time of the two parts of the velocity of the earth, we shall have the actual apparent position, which describes a little ellipse around the mean apparent position, and it is this ellipse that we observe.

Neglecting very small quantities, we shall see that the dimensions of this ellipse depend only upon the ratio of the velocity of the earth with reference to the sun to the velocity of light, so that the relative velocity of the earth with regard to the sun has alone come in.

But wait! This result is not exact, it is only approximate; let us push the approximation a little farther. The dimensions of the ellipse will depend then upon the absolute velocity of the earth. Let us compare the major axes of the ellipse for the different stars: we shall have, theoretically at least, the means of determining this absolute velocity.

That would be perhaps less shocking than it at first seems; it is a question, in fact, not of the velocity with
reference to an absolute void, but of the velocity with regard to the ether, which is taken *by definition* as
being absolutely at rest.

Besides, this method is purely theoretical. In fact, the aberration is very small; the possible variations of the ellipse of aberration are much smaller yet, and, if we consider the aberration as of the first order, they should therefore be regarded as of the second order: about a millionth of a second; they are absolutely inappreciable for our instruments. We shall finally see, further on, why the preceding theory should be rejected, and why we could not determine this absolute velocity even if our instruments were ten thousand times more precise!

One might imagine some other means, and in fact, so one has. The velocity of light is not the same in water as in air; could we not compare the two apparent positions of a star seen through a telescope first full of air, then full of water? The results have been negative; the apparent laws of reflection and refraction are not altered by the motion of the earth. This phenomenon is capable of two explanations:

1º It might be supposed that the ether is not at rest, but that it is carried along by the
body in motion. It would then not be astonishing that the phenomena of refraction are not altered by the motion of the
earth, since all, prisms, telescopes and ether, are carried along together in the same translation. As to the
aberration itself, it would be explained by a sort of refraction happening at the surface of separation of the ether at
rest in the interstellar spaces and the ether carried along by the motion of the earth. It is upon this hypothesis
(bodily carrying along of the ether) that is founded the *theory of Hertz* on the electrodynamics of moving
bodies.

2º Fresnel, on the contrary, supposes that the ether is at absolute rest in the void, at rest almost absolute in the
air, whatever be the velocity of this air, and that it is partially carried along by refractive media. Lorentz has
given to this theory a more satisfactory form. For him, the ether is at rest, only the electrons are in motion; in the
void, where it is only a question of the ether, in the air, where this is almost the case, the carrying along is null
or almost null; in refractive media, where perturbation is produced at the same time by vibrations of the ether and
those of electrons put in swing by the agitation of the ether, the undulations are *partially* carried
along.

To decide between the two hypotheses, we have Fizeau’s experiment, comparing by measurements of the fringes of
interference, the velocity of light in air at rest or in motion. These experiments have confirmed Fresnel’s hypothesis
of partial carrying along. They have been repeated with the same result by Michelson. *The theory of Hertz must
therefore be rejected.*

But if the ether is not carried along by the motion of the earth, is it possible to show, by means of optical phenomena, the absolute velocity of the earth, or rather its velocity with respect to the unmoving ether? Experiment has answered negatively, and yet the experimental procedures have been varied in all possible ways. Whatever be the means employed there will never be disclosed anything but relative velocities; I mean the velocities of certain material bodies with reference to other material bodies. In fact, if the source of light and the apparatus of observation are on the earth and participate in its motion, the experimental results have always been the same, whatever be the orientation of the apparatus with reference to the orbital motion of the earth. If astronomic aberration happens, it is because the source, a star, is in motion with reference to the observer.

The hypotheses so far made perfectly account for this general result, *if we neglect very small quantities of the
order of the square of the aberration*. The explanation rests upon the notion of *local time*, introduced by
Lorentz, which I shall try to make clear. Suppose two observers, placed one at *A*, the other at *B*, and
wishing to set their watches by means of optical signals. They agree that *B* shall send a signal to *A*
when his watch marks an hour determined upon, and *A* is to put his watch to that hour the moment he sees the
signal. If this alone were done, there would be a systematic error, because as the light takes a certain time
*t* to go from *B* to *A*, *A*‘s watch would be behind *B*‘s the time *t*.
This error is easily corrected. It suffices to cross the signals. *A* in turn must signal *B*, and, after
this new adjustment, *B*‘s watch will be behind *A*‘s the time *t*. Then it will be sufficient to
take the arithmetic mean of the two adjustments.

But this way of doing supposes that light takes the same time to go from *A* to *B* as to return from
*B* to *A*. That is true if the observers are motionless; it is no longer so if they are carried along in
a common translation, since then *A*, for example, will go to meet the light coming from *B*, while
*B* will flee before the light coming from *A*. If therefore the observers are borne along in a common
translation and if they do not suspect it, their adjustment will be defective; their watches will not indicate the same
time; each will show the *local time* belonging to the point where it is.

The two observers will have no way of perceiving this, if the unmoving ether can transmit to them only luminous signals all of the same velocity, and if the other signals they might send are transmitted by media carried along with them in their translation. The phenomenon each observes will be too soon or too late; it would be seen at the same instant only if the translation did not exist; but as it will be observed with a watch that is wrong, this will not be perceived and the appearances will not be altered.

It results from this that the compensation is easy to explain so long as we neglect the square of the aberration,
and for a long time the experiments were not sufficiently precise to warrant taking account of it. But the day came
when Michelson imagined a much more delicate procedure: he made rays interfere which had traversed different courses,
after being reflected by mirrors; each of the paths approximating a meter and the fringes of interference permitting
the recognition of a fraction of a thousandth of a millimeter, the square of the aberration could no longer be
neglected, and *yet the results were still negative*. Therefore the theory required to be completed, and it has
been by the *Lorentz-Fitzgerald hypothesis*.

These two physicists suppose that all bodies carried along in a translation undergo a contraction in the sense of
this translation, while their dimensions perpendicular to this translation remain unchanged. *This contraction is
the same for all bodies*; moreover, it is very slight, about one two-hundred-millionth for a velocity such as that
of the earth. Furthermore our measuring instruments could not disclose it, even if they were much more precise; our
measuring rods in fact undergo the same contraction as the objects to be measured. If the meter exactly fits when
applied to a body, if we point the body and consequently the meter in the sense of the motion of the earth, it will not
cease to exactly fit in another orientation, and that although the body and the meter have changed in length as well as
orientation, and precisely because the change is the same for one as for the other. But it is quite different if we
measure a length, not now with a meter, but by the time taken by light to pass along it, and this is just what
Michelson has done.

A body, spherical when at rest, will take thus the form of a flattened ellipsoid of revolution when in motion; but the observer will always think it spherical, since he himself has undergone an analogous deformation, as also all the objects serving as points of reference. On the contrary, the surfaces of the waves of light, remaining rigorously spherical, will seem to him elongated ellipsoids.

What happens then? Suppose an observer and a source of light carried along together in the translation: the wave
surfaces emanating from the source will be spheres having as centers the successive positions of the source; the
distance from this center to the actual position of the source will be proportional to the time elapsed after the
emission, that is to say to the radius of the sphere. All these spheres are therefore homothetic one to the other, with
relation to the actual position *S* of the source. But, for our observer, because of the contraction, all these
spheres will seem elongated ellipsoids, and all these ellipsoids will moreover be homothetic, with reference to the
point *S*; the excentricity of all these ellipsoids is the same and depends solely upon the velocity of the
earth. *We shall so select the law of contraction that the point S may be at the focus of the meridian section of
the ellipsoid.*

This time the compensation is *rigorous*, and this it is which explains Michelson’s experiment.

I have said above that, according to the ordinary theories, observations of the astronomic aberration would give us
the absolute velocity of the earth, if our instruments were a thousand times more precise. I must modify this
statement. Yes, the observed angles would be modified by the effect of this absolute velocity, but the graduated
circles we use to measure the angles would be deformed by the translation: they would become ellipses; thence would
result an error in regard to the angle measured, and *this second error would exactly compensate the first*.

This Lorentz-Fitzgerald hypothesis seems at first very extraordinary; all we can say for the moment, in its favor,
is that it is only the immediate translation of Michelson’s experimental result, if we *define* lengths by the
time taken by light to run along them.

However that may be, it is impossible to escape the impression that the principle of relativity is a general law of nature, that one will never be able by any imaginable means to show any but relative velocities, and I mean by that not only the velocities of bodies with reference to the ether, but the velocities of bodies with regard to one another. Too many different experiments have given concordant results for us not to feel tempted to attribute to this principle of relativity a value comparable to that, for example, of the principle of equivalence. In any case, it is proper to see to what consequences this way of looking at things would lead us and then to submit these consequences to the control of experiment.

Let us see what the principle of the equality of action and reaction becomes in the theory of Lorentz. Consider an
electron *A* which for any cause begins to move; it produces a perturbation in the ether; at the end of a
certain time, this perturbation reaches another electron *B*, which will be disturbed from its position of
equilibrium. In these conditions there can not be equality between action and reaction, at least if we do not consider
the ether, but only the electrons, *which alone are observable*, since our matter is made of electrons.

In fact it is the electron *A* which has disturbed the electron *B*; even in case the electron
*B* should react upon *A*, this reaction could be equal to the action, but in no case simultaneous, since
the electron *B* can begin to move only after a certain time, necessary for the propagation. Submitting the
problem to a more exact calculation, we reach the following result: Suppose a Hertz discharger placed at the focus of a
parabolic mirror to which it is mechanically attached; this discharger emits electromagnetic waves, and the mirror
reflects all these waves in the same direction; the discharger therefore will radiate energy in a determinate
direction. Well, the calculation shows that *the discharger recoils* like a cannon which has shot out a
projectile. In the case of the cannon, the recoil is the natural result of the equality of action and reaction. The
cannon recoils because the projectile upon which it has acted reacts upon it. But here it is no longer the same. What
has been sent out is no longer a material projectile: it is energy, and energy has no mass: it has no counterpart. And, in place of a discharger, we could have considered just simply a lamp with a
reflector concentrating its rays in a single direction.

It is true that, if the energy sent out from the discharger or from the lamp meets a material object, this object receives a mechanical push as if it had been hit by a real projectile, and this push will be equal to the recoil of the discharger and of the lamp, if no energy has been lost on the way and if the object absorbs the whole of the energy. Therefore one is tempted to say that there still is compensation between the action and the reaction. But this compensation, even should it be complete, is always belated. It never happens if the light, after leaving its source, wanders through interstellar spaces without ever meeting a material body; it is incomplete, if the body it strikes is not perfectly absorbent.

Are these mechanical actions too small to be measured, or are they accessible to experiment? These actions are
nothing other than those due to the *Maxwell-Bartholi* pressures; Maxwell had predicted these pressures from
calculations relative to electrostatics and magnetism; Bartholi reached the same result by thermodynamic
considerations.

This is how the *tails of comets* are explained. Little particles detach themselves from the nucleus of the
comet; they are struck by the light of the sun, which pushes them back as would a rain of projectiles coming from the
sun. The mass of these particles is so little that this repulsion sweeps it away against the Newtonian attraction; so
in moving away from the sun they form the tails.

The direct experimental verification was not easy to obtain. The first endeavor led to the construction of the
*radiometer*. But this instrument *turns backward*, in the sense opposite to the theoretic sense, and the
explanation of its rotation, since discovered, is wholly different. At last success came, by making the vacuum more
complete, on the one hand, and on the other by not blackening one of the faces of the paddles and directing a pencil of
luminous rays upon one of the faces. The radiometric effects and the other disturbing causes are eliminated by a series
of pains-taking precautions, and one obtains a deviation which is very minute, but which is, it
would seem, in conformity with the theory.

The same effects of the Maxwell-Bartholi pressure are forecast likewise by the theory of Hertz of which we have before spoken, and by that of Lorentz. But there is a difference. Suppose that the energy, under the form of light, for example, proceeds from a luminous source to any body through a transparent medium. The Maxwell-Bartholi pressure will act, not alone upon the source at the departure, and on the body lit up at the arrival, but upon the matter of the transparent medium which it traverses. At the moment when the luminous wave reaches a new region of this medium, this pressure will push forward the matter there distributed and will put it back when the wave leaves this region. So that the recoil of the source has for counterpart the forward movement of the transparent matter which is in contact with this source; a little later, the recoil of this same matter has for counterpart the forward movement of the transparent matter which lies a little further on, and so on.

Only, is the compensation perfect? Is the action of the Maxwell-Bartholi pressure upon the matter of the transparent medium equal to its reaction upon the source, and that whatever be this matter? Or is this action by so much the less as the medium is less refractive and more rarefied, becoming null in the void?

If we admit the theory of Hertz, who regards matter as mechanically bound to the ether, so that the ether may be entirely carried along by matter, it would be necessary to answer yes to the first question and no to the second.

There would then be perfect compensation, as required by the principle of the equality of action and reaction, even in the least refractive media, even in the air, even in the interplanetary void, where it would suffice to suppose a residue of matter, however subtile. If on the contrary we admit the theory of Lorentz, the compensation, always imperfect, is insensible in the air and becomes null in the void.

But we have seen above that Fizeau’s experiment does not permit of our retaining the theory of Hertz; it is
necessary therefore to adopt the theory of Lorentz, and consequently *to renounce the
principle of reaction*.

We have seen above the reasons which impel us to regard the principle of relativity as a general law of nature. Let us see to what consequences this principle would lead, should it be regarded as finally demonstrated.

First, it obliges us to generalize the hypothesis of Lorentz and Fitzgerald on the contraction of all bodies in the sense of the translation. In particular, we must extend this hypothesis to the electrons themselves. Abraham considered these electrons as spherical and indeformable; it will be necessary for us to admit that these electrons, spherical when in repose, undergo the Lorentz contraction when in motion and take then the form of flattened ellipsoids.

This deformation of the electrons will influence their mechanical properties. In fact I have said that the displacement of these charged electrons is a veritable current of convection and that their apparent inertia is due to the self-induction of this current: exclusively as concerns the negative electrons; exclusively or not, we do not yet know, for the positive electrons. Well, the deformation of the electrons, a deformation which depends upon their velocity, will modify the distribution of the electricity upon their surface, consequently the intensity of the convection current they produce, consequently the laws according to which the self-induction of this current will vary as a function of the velocity.

At this price, the compensation will be perfect and will conform to the requirements of the principle of relativity, but only upon two conditions:

1º That the positive electrons have no real mass, but only a fictitious electromagnetic mass; or at least that their real mass, if it exists, is not constant and varies with the velocity according to the same laws as their fictitious mass;

2º That all forces are of electromagnetic origin, or at least that they vary with the velocity according to the same laws as the forces of electromagnetic origin.

It still is Lorentz who has made this remarkable synthesis; stop a moment and see what follows therefrom. First, there is no more matter, since the positive electrons no longer have real mass, or at least no constant real mass. The present principles of our mechanics, founded upon the constancy of mass, must therefore be modified. Again, an electromagnetic explanation must be sought of all the known forces, in particular of gravitation, or at least the law of gravitation must be so modified that this force is altered by velocity in the same way as the electromagnetic forces. We shall return to this point.

All that appears, at first sight, a little artificial. In particular, this deformation of electrons seems quite
hypothetical. But the thing may be presented otherwise, so as to avoid putting this hypothesis of deformation at the
foundation of the reasoning. Consider the electrons as material points and ask how their mass should vary as function
of the velocity not to contravene the principle of relativity. Or, still better, ask what should be their acceleration
under the influence of an electric or magnetic field, that this principle be not violated and that we come back to the
ordinary laws when we suppose the velocity very slight. We shall find that the variations of this mass, or of these
accelerations, must be *as if* the electron underwent the Lorentz deformation.

We have before us, then, two theories: one where the electrons are indeformable, this is that of Abraham; the other where they undergo the Lorentz deformation. In both cases, their mass increases with the velocity, becoming infinite when this velocity becomes equal to that of light; but the law of the variation is not the same. The method employed by Kaufmann to bring to light the law of variation of the mass seems therefore to give us an experimental means of deciding between the two theories.

Unhappily, his first experiments were not sufficiently precise for that; so he decided to repeat them with more
precautions, and measuring with great care the intensity of the fields. Under their new form
*they are in favor of the theory of Abraham*. Then the principle of relativity would not have the rigorous value
we were tempted to attribute to it; there would no longer be reason for believing the positive electrons denuded of
real mass like the negative electrons. However, before definitely adopting this conclusion, a little reflection is
necessary. The question is of such importance that it is to be wished Kaufmann’s experiment were repeated by another
experimenter.^{17} Unhappily, this experiment is very delicate and could be
carried out successfully only by a physicist of the same ability as Kaufmann. All precautions have been properly taken
and we hardly see what objection could be made.

There is one point however to which I wish to draw attention: that is to the measurement of the electrostatic field, a measurement upon which all depends. This field was produced between the two armatures of a condenser; and, between these armatures, there was to be made an extremely perfect vacuum, in order to obtain a complete isolation. Then the difference of potential of the two armatures was measured, and the field obtained by dividing this difference by the distance apart of the armatures. That supposes the field uniform; is this certain? Might there not be an abrupt fall of potential in the neighborhood of one of the armatures, of the negative armature, for example? There may be a difference of potential at the meeting of the metal and the vacuum, and it may be that this difference is not the same on the positive side and on the negative side; what would lead me to think so is the electric valve effects between mercury and vacuum. However slight the probability that it is so, it seems that it should be considered.

^{17} At the moment of going to press we learn that M. Bucherer has repeated
the experiment, taking new precautions, and that he has obtained, contrary to Kaufmann, results confirming the views of
Lorentz.

In the new dynamics, the principle of inertia is still true, that is to say that an *isolated* electron will
have a straight and uniform motion. At least this is generally assumed; however, Lindemann has
made objections to this view; I do not wish to take part in this discussion, which I can not here expound because of
its too difficult character. In any case, slight modifications to the theory would suffice to shelter it from
Lindemann’s objections.

We know that a body submerged in a fluid experiences, when in motion, considerable resistance, but this is because our fluids are viscous; in an ideal fluid, perfectly free from viscosity, the body would stir up behind it a liquid hill, a sort of wake; upon departure, a great effort would be necessary to put it in motion, since it would be necessary to move not only the body itself, but the liquid of its wake. But, the motion once acquired, it would perpetuate itself without resistance, since the body, in advancing, would simply carry with it the perturbation of the liquid, without the total vis viva of the liquid augmenting. Everything would happen therefore as if its inertia was augmented. An electron advancing in the ether would behave in the same way: around it, the ether would be stirred up, but this perturbation would accompany the body in its motion; so that, for an observer carried along with the electron, the electric and magnetic fields accompanying this electron would appear invariable, and would change only if the velocity of the electron varied. An effort would therefore be necessary to put the electron in motion, since it would be necessary to create the energy of these fields; on the contrary, once the movement acquired, no effort would be necessary to maintain it, since the created energy would only have to go along behind the electron as a wake. This energy, therefore, could only augment the inertia of the electron, as the agitation of the liquid augments that of the body submerged in a perfect fluid. And anyhow, the negative electrons at least have no other inertia except that.

In the hypothesis of Lorentz, the vis viva, which is only the energy of the ether, is not proportional to
*v*^{2}. Doubtless if *v* is very slight, the vis viva is sensibly proportional to
*v*^{2}, the quantity of motion sensibly proportional to *v*, the two masses sensibly constant
and equal to each other. But *when the velocity tends toward the velocity of light, the vis viva, the quantity of
motion and the two masses increase beyond all limit*.

In the hypothesis of Abraham, the expressions are a little more complicated; but what we have just said remains true in essentials.

So the mass, the quantity of motion, the vis viva become infinite when the velocity is equal to that of light.

Thence results that *no body can attain in any way a velocity beyond that of light*. And in fact, in
proportion as its velocity increases, its mass increases, so that its inertia opposes to any new increase of velocity a
greater and greater obstacle.

A question then suggests itself: let us admit the principle of relativity; an observer in motion would not have any means of perceiving his own motion. If therefore no body in its absolute motion can exceed the velocity of light, but may approach it as nearly as you choose, it should be the same concerning its relative motion with reference to our observer. And then we might be tempted to reason as follows: The observer may attain a velocity of 200,000 kilometers; the body in its relative motion with reference to the observer may attain the same velocity; its absolute velocity will then be 400,000 kilometers, which is impossible, since this is beyond the velocity of light. This is only a seeming, which vanishes when account is taken of how Lorentz evaluates local time.

When an electron is in motion, it produces a perturbation in the ether surrounding it; if its motion is straight and
uniform, this perturbation reduces to the wake of which we have spoken in the preceding section. But it is no longer
the same, if the motion be curvilinear or varied. The perturbation may then be regarded as the superposition of two
others, to which Langevin has given the names *wave of velocity* and *wave of acceleration*. The wave of
velocity is only the wave which happens in uniform motion.

As to the wave of acceleration, this is a perturbation altogether analogous to light waves, which starts from the electron at the instant when it undergoes an acceleration, and which is then propagated by successive spherical waves with the velocity of light. Whence follows: in a straight and uniform motion, the energy is wholly conserved; but, when there is an acceleration, there is loss of energy, which is dissipated under the form of luminous waves and goes out to infinity across the ether.

However, the effects of this wave of acceleration, in particular the corresponding loss of energy, are in most cases
negligible, that is to say not only in ordinary mechanics and in the motions of the heavenly bodies, but even in the
radium rays, where the velocity is very great without the acceleration being so. We may then confine ourselves to
applying the laws of mechanics, putting the force equal to the product of acceleration by mass, this mass, however,
varying with the velocity according to the laws explained above. We then say the motion is
*quasi-stationary*.

It would not be the same in all cases where the acceleration is great, of which the chief are the following:

1º In incandescent gases certain electrons take an oscillatory motion of very high frequency; the displacements are very small, the velocities are finite, and the accelerations very great; energy is then communicated to the ether, and this is why these gases radiate light of the same period as the oscillations of the electron;

2º Inversely, when a gas receives light, these same electrons are put in swing with strong accelerations and they absorb light;

3º In the Hertz discharger, the electrons which circulate in the metallic mass undergo, at the instant of the discharge, an abrupt acceleration and take then an oscillatory motion of high frequency. Thence results that a part of the energy radiates under the form of Hertzian waves;

4º In an incandescent metal, the electrons enclosed in this metal are impelled with great velocity; upon reaching the surface of the metal, which they can not get through, they are reflected and thus undergo a considerable acceleration. This is why the metal emits light. The details of the laws of the emission of light by dark bodies are perfectly explained by this hypothesis;

5º Finally when the cathode rays strike the anticathode, the negative electrons, constituting these rays, which are impelled with very great velocity, are abruptly arrested. Because of the acceleration they thus undergo, they produce undulations in the ether. This, according to certain physicists, is the origin of the Röntgen rays, which would only be light rays of very short wave-length.

Mass may be defined in two ways:

1º By the quotient of the force by the acceleration; this is the true definition of the mass, which measures the inertia of the body.

2º By the attraction the body exercises upon an exterior body, in virtue of Newton’s law. We should therefore distinguish the mass coefficient of inertia and the mass coefficient of attraction. According to Newton’s law, there is rigorous proportionality between these two coefficients. But that is demonstrated only for velocities to which the general principles of dynamics are applicable. Now, we have seen that the mass coefficient of inertia increases with the velocity; should we conclude that the mass coefficient of attraction increases likewise with the velocity and remains proportional to the coefficient of inertia, or, on the contrary, that this coefficient of attraction remains constant? This is a question we have no means of deciding.

On the other hand, if the coefficient of attraction depends upon the velocity, since the velocities of two bodies which mutually attract are not in general the same, how will this coefficient depend upon these two velocities?

Upon this subject we can only make hypotheses, but we are naturally led to investigate which of these hypotheses would be compatible with the principle of relativity. There are a great number of them; the only one of which I shall here speak is that of Lorentz, which I shall briefly expound.

Consider first electrons at rest. Two electrons of the same sign repel each other and two electrons of contrary sign
attract each other; in the ordinary theory, their mutual actions are proportional to their electric charges; if
therefore we have four electrons, two positive *A* and *A´*, and two negative
*B* and *B´*, the charges of these four being the same in absolute value, the repulsion of *A* for
*A´* will be, at the same distance, equal to the repulsion of *B* for *B´* and equal also to the
attraction of *A* for *B´*, or of *A´* for *B*. If therefore *A* and *B* are
very near each other, as also *A´* and *B´*, and we examine the action of the system *A* +
*B* upon the system *A´* + *B´*, we shall have two repulsions and two attractions which will
exactly compensate each other and the resulting action will be null.

Now, material molecules should just be regarded as species of solar systems where circulate the electrons, some
positive, some negative, and *in such a way that the algebraic sum of all the charges is null*. A material
molecule is therefore wholly analogous to the system *A* + *B* of which we have spoken, so that the total
electric action of two molecules one upon the other should be null.

But experiment shows us that these molecules attract each other in consequence of Newtonian gravitation; and then we may make two hypotheses: we may suppose gravitation has no relation to the electrostatic attractions, that it is due to a cause entirely different, and is simply something additional; or else we may suppose the attractions are not proportional to the charges and that the attraction exercised by a charge +1 upon a charge −1 is greater than the mutual repulsion of two +1 charges, or two −1 charges.

In other words, the electric field produced by the positive electrons and that which the negative electrons produce might be superposed and yet remain distinct. The positive electrons would be more sensitive to the field produced by the negative electrons than to the field produced by the positive electrons; the contrary would be the case for the negative electrons. It is clear that this hypothesis somewhat complicates electrostatics, but that it brings back into it gravitation. This was, in sum, Franklin’s hypothesis.

What happens now if the electrons are in motion? The positive electrons will cause a perturbation in the ether and produce there an electric and magnetic field. The same will be the case for the negative electrons. The electrons, positive as well as negative, undergo then a mechanical impulsion by the action of these different fields. In the ordinary theory, the electromagnetic field, due to the motion of the positive electrons, exercises, upon two electrons of contrary sign and of the same absolute charge, equal actions with contrary sign. We may then without inconvenience not distinguish the field due to the motion of the positive electrons and the field due to the motion of the negative electrons and consider only the algebraic sum of these two fields, that is to say the resulting field.

In the new theory, on the contrary, the action upon the positive electrons of the electromagnetic field due to the
positive electrons follows the ordinary laws; it is the same with the action upon the negative electrons of the field
due to the negative electrons. Let us now consider the action of the field due to the positive electrons upon the
negative electrons (or inversely); it will still follow the same laws, but *with a different coefficient*. Each
electron is more sensitive to the field created by the electrons of contrary name than to the field created by the
electrons of the same name.

Such is the hypothesis of Lorentz, which reduces to Franklin’s hypothesis for slight velocities; it will therefore explain, for these small velocities, Newton’s law. Moreover, as gravitation goes back to forces of electrodynamic origin, the general theory of Lorentz will apply, and consequently the principle of relativity will not be violated.

We see that Newton’s law is no longer applicable to great velocities and that it must be modified, for bodies in motion, precisely in the same way as the laws of electrostatics for electricity in motion.

We know that electromagnetic perturbations spread with the velocity of light. We may therefore be tempted to reject the preceding theory upon remembering that gravitation spreads, according to the calculations of Laplace, at least ten million times more quickly than light, and that consequently it can not be of electromagnetic origin. The result of Laplace is well known, but one is generally ignorant of its signification. Laplace supposed that, if the propagation of gravitation is not instantaneous, its velocity of spread combines with that of the body attracted, as happens for light in the phenomenon of astronomic aberration, so that the effective force is not directed along the straight joining the two bodies, but makes with this straight a small angle. This is a very special hypothesis, not well justified, and, in any case, entirely different from that of Lorentz. Laplace’s result proves nothing against the theory of Lorentz.

Can the preceding theories be reconciled with astronomic observations?

First of all, if we adopt them, the energy of the planetary motions will be constantly dissipated by the effect of
the *wave of acceleration*. From this would result that the mean motions of the stars would constantly
accelerate, as if these stars were moving in a resistant medium. But this effect is exceedingly slight, far too much so
to be discerned by the most precise observations. The acceleration of the heavenly bodies is relatively slight, so that
the effects of the wave of acceleration are negligible and the motion may be regarded as *quasi stationary*. It
is true that the effects of the wave of acceleration constantly accumulate, but this accumulation itself is so slow
that thousands of years of observation would be necessary for it to become sensible. Let us therefore make the
calculation considering the motion as quasi-stationary, and that under the three following hypotheses:

A. Admit the hypothesis of Abraham (electrons indeformable) and retain Newton’s law in its usual form;

B. Admit the hypothesis of Lorentz about the deformation of electrons and retain the usual Newton’s law;

C. Admit the hypothesis of Lorentz about electrons and modify Newton’s law as we have done in the preceding paragraph, so as to render it compatible with the principle of relativity.

It is in the motion of Mercury that the effect will be most sensible, since this planet has the greatest velocity. Tisserand formerly made an analogous calculation, admitting Weber’s law; I recall that Weber had sought to explain at the same time the electrostatic and electrodynamic phenomena in supposing that electrons (whose name was not yet invented) exercise, one upon another, attractions and repulsions directed along the straight joining them, and depending not only upon their distances, but upon the first and second derivatives of these distances, consequently upon their velocities and their accelerations. This law of Weber, different enough from those which to-day tend to prevail, none the less presents a certain analogy with them.

Tisserand found that, if the Newtonian attraction conformed to Weber’s law there resulted, for Mercury’s perihelion,
secular variation of 14´´, *of the same sense as that which has been observed and could not be explained*, but
smaller, since this is 38´´.

Let us recur to the hypotheses A, B and C, and study first the motion of a planet attracted by a fixed center. The hypotheses B and C are no longer distinguished, since, if the attracting point is fixed, the field it produces is a purely electrostatic field, where the attraction varies inversely as the square of the distance, in conformity with Coulomb’s electrostatic law, identical with that of Newton.

The vis viva equation holds good, taking for vis viva the new definition; in the same way, the equation of areas is replaced by another equivalent to it; the moment of the quantity of motion is a constant, but the quantity of motion must be defined as in the new dynamics.

The only sensible effect will be a secular motion of the perihelion. With the theory of Lorentz, we shall find, for this motion, half of what Weber’s law would give; with the theory of Abraham, two fifths.

If now we suppose two moving bodies gravitating around their common center of gravity, the effects are very little different, though the calculations may be a little more complicated. The motion of Mercury’s perihelion would therefore be 7´´ in the theory of Lorentz and 5´´.6 in that of Abraham.

The effect moreover is proportional to *n*^{3}*a*^{2}, where *n* is the star’s
mean motion and a the radius of its orbit. For the planets, in virtue of Kepler’s law, the effect varies then inversely
as √*a*^{5}; it is therefore insensible, save for Mercury.

It is likewise insensible for the moon though *n* is great, because *a* is extremely small; in sum, it
is five times less for Venus, and six hundred times less for the moon than for Mercury. We may add that as to Venus and
the earth, the motion of the perihelion (for the same angular velocity of this motion) would be much more difficult to
discern by astronomic observations, because the excentricity of their orbits is much less than for Mercury.

To sum up, *the only sensible effect upon astronomic observations would be a motion of Mercury’s perihelion, in
the same sense as that which has been observed without being explained, but notably slighter*.

That can not be regarded as an argument in favor of the new dynamics, since it will always be necessary to seek another explanation for the greater part of Mercury’s anomaly; but still less can it be regarded as an argument against it.

It is interesting to compare these considerations with a theory long since proposed to explain universal gravitation.

Suppose that, in the interplanetary spaces, circulate in every direction, with high velocities, very tenuous
corpuscles. A body isolated in space will not be affected, apparently, by the impacts of these corpuscles, since these
impacts are equally distributed in all directions. But if two bodies *A* and *B* are present, the body
*B* will play the rôle of screen and will intercept part of the corpuscles which, without it, would have struck
*A*. Then, the impacts received by *A* in the direction opposite that from *B* will no longer have
a counterpart, or will now be only partially compensated, and this will push *A* toward *B*.

Such is the theory of Lesage; and we shall discuss it, taking first the view-point of ordinary mechanics.

First, how should the impacts postulated by this theory take place; is it according to the laws of perfectly elastic
bodies, or according to those of bodies devoid of elasticity, or according to an intermediate law? The corpuscles of
Lesage can not act as perfectly elastic bodies; otherwise the effect would be null, since the
corpuscles intercepted by the body *B* would be replaced by others which would have rebounded from *B*,
and calculation proves that the compensation would be perfect. It is necessary then that the impact make the corpuscles
lose energy, and this energy should appear under the form of heat. But how much heat would thus be produced? Note that
attraction passes through bodies; it is necessary therefore to represent to ourselves the earth, for example, not as a
solid screen, but as formed of a very great number of very small spherical molecules, which play individually the rôle
of little screens, but between which the corpuscles of Lesage may freely circulate. So, not only the earth is not a
solid screen, but it is not even a cullender, since the voids occupy much more space than the plenums. To realize this,
recall that Laplace has demonstrated that attraction, in traversing the earth, is weakened at most by one ten-millionth
part, and his proof is perfectly satisfactory: in fact, if attraction were absorbed by the body it traverses, it would
no longer be proportional to the masses; it would be *relatively* weaker for great bodies than for small, since
it would have a greater thickness to traverse. The attraction of the sun for the earth would therefore be
*relatively* weaker than that of the sun for the moon, and thence would result, in the motion of the moon, a
very sensible inequality. We should therefore conclude, if we adopt the theory of Lesage, that the total surface of the
spherical molecules which compose the earth is at most the ten-millionth part of the total surface of the earth.

Darwin has proved that the theory of Lesage only leads exactly to Newton’s law when we postulate particles entirely
devoid of elasticity. The attraction exerted by the earth on a mass 1 at a distance 1 will then be proportional, at the
same time, to the total surface *S* of the spherical molecules composing it, to the velocity *v* of the
corpuscles, to the square root of the density ρ of the medium formed by the corpuscles. The heat produced will be
proportional to *S*, to the density ρ, and to the cube of the velocity *v*.

But it is necessary to take account of the resistance experienced by a body moving in such a medium; it can not
move, in fact, without going against certain impacts, in fleeing, on the contrary, before those
coming in the opposite direction, so that the compensation realized in the state of rest can no longer subsist. The
calculated resistance is proportional to *S*, to ρ and to *v*; now, we know that the heavenly bodies move
as if they experienced no resistance, and the precision of observations permits us to fix a limit to the resistance of
the medium.

This resistance varying as *S*ρ*v*, while the attraction varies as *S*√(ρ*v*), we see
that the ratio of the resistance to the square of the attraction is inversely as the product *Sv*.

We have therefore a lower limit of the product *Sv*. We have already an upper limit of *S* (by the
absorption of attraction by the body it traverses); we have therefore a lower limit of the velocity *v*, which
must be at least 24·10^{17} times that of light.

From this we are able to deduce ρ and the quantity of heat produced; this quantity would suffice to raise the
temperature 10^{26} degrees a second; the earth would receive in a given time 10^{20} times more heat
than the sun emits in the same time; I am not speaking of the heat the sun sends to the earth, but of that it radiates
in all directions.

It is evident the earth could not long stand such a régime.

We should not be led to results less fantastic if, contrary to Darwin’s views, we endowed the corpuscles of Lesage with an elasticity imperfect without being null. In truth, the vis viva of these corpuscles would not be entirely converted into heat, but the attraction produced would likewise be less, so that it would be only the part of this vis viva converted into heat, which would contribute to produce the attraction and that would come to the same thing; a judicious employment of the theorem of the viriel would enable us to account for this.

The theory of Lesage may be transformed; suppress the corpuscles and imagine the ether overrun in all senses by luminous waves coming from all points of space. When a material object receives a luminous wave, this wave exercises upon it a mechanical action due to the Maxwell-Bartholi pressure, just as if it had received the impact of a material projectile. The waves in question could therefore play the rôle of the corpuscles of Lesage. This is what is supposed, for example, by M. Tommasina.

The difficulties are not removed for all that; the velocity of propagation can be only that of light, and we are thus led, for the resistance of the medium, to an inadmissible figure. Besides, if the light is all reflected, the effect is null, just as in the hypothesis of the perfectly elastic corpuscles.

That there should be attraction, it is necessary that the light be partially absorbed; but then there is production of heat. The calculations do not differ essentially from those made in the ordinary theory of Lesage, and the result retains the same fantastic character.

On the other hand, attraction is not absorbed by the body it traverses, or hardly at all; it is not so with the light we know. Light which would produce the Newtonian attraction would have to be considerably different from ordinary light and be, for example, of very short wave length. This does not count that, if our eyes were sensible of this light, the whole heavens should appear to us much more brilliant than the sun, so that the sun would seem to us to stand out in black, otherwise the sun would repel us instead of attracting us. For all these reasons, light which would permit of the explanation of attraction would be much more like Röntgen rays than like ordinary light.

And besides, the X-rays would not suffice; however penetrating they may seem to us, they could not pass through the whole earth; it would be necessary therefore to imagine X´-rays much more penetrating than the ordinary X-rays. Moreover a part of the energy of these X´-rays would have to be destroyed, otherwise there would be no attraction. If you do not wish it transformed into heat, which would lead to an enormous heat production, you must suppose it radiated in every direction under the form of secondary rays, which might be called X´´ and which would have to be much more penetrating still than the X´-rays, otherwise they would in their turn derange the phenomena of attraction.

Such are the complicated hypotheses to which we are led when we try to give life to the theory of Lesage.

But all we have said presupposes the ordinary laws of mechanics.

Will things go better if we admit the new dynamics? And first, can we conserve the principles of relativity? Let us give at first to the theory of Lesage its primitive form, and suppose space ploughed by material corpuscles; if these corpuscles were perfectly elastic, the laws of their impact would conform to this principle of relativity, but we know that then their effect would be null. We must therefore suppose these corpuscles are not elastic, and then it is difficult to imagine a law of impact compatible with the principle of relativity. Besides, we should still find a production of considerable heat, and yet a very sensible resistance of the medium.

If we suppress these corpuscles and revert to the hypothesis of the Maxwell-Bartholi pressure, the difficulties will not be less. This is what Lorentz himself has attempted in his Memoir to the Amsterdam Academy of Sciences of April 25, 1900.

Consider a system of electrons immersed in an ether permeated in every sense by luminous waves; one of these
electrons, struck by one of these waves, begins to vibrate; its vibration will be synchronous with that of light; but
it may have a difference of phase, if the electron absorbs a part of the incident energy. In fact, if it absorbs
energy, this is because the vibration of the ether *impels* the electron; the electron must therefore be slower
than the ether. An electron in motion is analogous to a convection current; therefore every magnetic field, in
particular that due to the luminous perturbation itself, must exert a mechanical action upon this electron. This action
is very slight; moreover, it changes sign in the current of the period; nevertheless, the mean action is not null if
there is a difference of phase between the vibrations of the electron and those of the ether. The mean action is
proportional to this difference, consequently to the energy absorbed by the electron. I can not here enter into the
detail of the calculations; suffice it to say only that the final result is an attraction of any two electrons, varying
inversely as the square of the distance and proportional to the energy absorbed by the two electrons.

Therefore there can not be attraction without absorption of light and, consequently, without production of heat, and
this it is which determined Lorentz to abandon this theory, which, at bottom, does not differ from that of
Lesage-Maxwell-Bartholi. He would have been much more dismayed still if he had pushed the
calculation to the end. He would have found that the temperature of the earth would have to increase 10^{12}
degrees a second.

I have striven to give in few words an idea as complete as possible of these new doctrines; I have sought to explain how they took birth; otherwise the reader would have had ground to be frightened by their boldness. The new theories are not yet demonstrated; far from it; only they rest upon an aggregate of probabilities sufficiently weighty for us not to have the right to treat them with disregard.

New experiments will doubtless teach us what we should finally think of them. The knotty point of the question lies in Kaufmann’s experiment and those that may be undertaken to verify it.

In conclusion, permit me a word of warning. Suppose that, after some years, these theories undergo new tests and triumph; then our secondary education will incur a great danger; certain professors will doubtless wish to make a place for the new theories.

Novelties are so attractive, and it is so hard not to seem highly advanced! At least there will be the wish to open vistas to the pupils and, before teaching them the ordinary mechanics, to let them know it has had its day and was at best good enough for that old dolt Laplace. And then they will not form the habit of the ordinary mechanics.

Is it well to let them know this is only approximative? Yes; but later, when it has penetrated to their very marrow, when they shall have taken the bent of thinking only through it, when there shall no longer be risk of their unlearning it, then one may, without inconvenience, show them its limits.

It is with the ordinary mechanics that they must live; this alone will they ever have to apply. Whatever be the progress of automobilism, our vehicles will never attain speeds where it is not true. The other is only a luxury, and we should think of the luxury only when there is no longer any risk of harming the necessary.

Astronomic Science

The considerations to be here developed have scarcely as yet drawn the attention of astronomers; there is hardly
anything to cite except an ingenious idea of Lord Kelvin’s, which has opened a new field of research, but still waits
to be followed out. Nor have I original results to impart, and all I can do is to give an idea of the problems
presented, but which no one hitherto has undertaken to solve. Every one knows how a large number of modern physicists
represent the constitution of gases; gases are formed of an innumerable multitude of molecules which, at high speeds,
cross and crisscross in every direction. These molecules probably act at a distance one upon another, but this action
decreases very rapidly with distance, so that their trajectories remain sensibly straight; they cease to be so only
when two molecules happen to pass very near to each other; in this case, their mutual attraction or repulsion makes
them deviate to right or left. This is what is sometimes called an impact; but the word *impact* is not to be
understood in its usual sense; it is not necessary that the two molecules come into contact, it suffices that they
approach sufficiently near each other for their mutual attractions to become sensible. The laws of the deviation they
undergo are the same as for a veritable impact.

It seems at first that the disorderly impacts of this innumerable dust can engender only an inextricable chaos before which analysis must recoil. But the law of great numbers, that supreme law of chance, comes to our aid; in presence of a semi-disorder, we must despair, but in extreme disorder, this statistical law reestablishes a sort of mean order where the mind can recover. It is the study of this mean order which constitutes the kinetic theory of gases; it shows us that the velocities of the molecules are equally distributed among all the directions, that the rapidity of these velocities varies from one molecule to another, but that even this variation is subject to a law called Maxwell’s law. This law tells us how many of the molecules move with such and such a velocity. As soon as the gas departs from this law, the mutual impacts of the molecules, in modifying the rapidity and direction of their velocities, tend to bring it promptly back. Physicists have striven, not without success, to explain in this way the experimental properties of gases; for example Mariotte’s law.

Consider now the milky way; there also we see an innumerable dust; only the grains of this dust are not atoms, they are stars; these grains move also with high velocities; they act at a distance one upon another, but this action is so slight at great distance that their trajectories are straight; and yet, from time to time, two of them may approach near enough to be deviated from their path, like a comet which has passed too near Jupiter. In a word, to the eyes of a giant for whom our suns would be as for us our atoms, the milky way would seem only a bubble of gas.

Such was Lord Kelvin’s leading idea. What may be drawn from this comparison? In how far is it exact? This is what we are to investigate together; but before reaching a definite conclusion, and without wishing to prejudge it, we foresee that the kinetic theory of gases will be for the astronomer a model he should not follow blindly, but from which he may advantageously draw inspiration. Up to the present, celestial mechanics has attacked only the solar system or certain systems of double stars. Before the assemblage presented by the milky way, or the agglomeration of stars, or the resolvable nebulae it recoils, because it sees therein only chaos. But the milky way is not more complicated than a gas; the statistical methods founded upon the calculus of probabilities applicable to a gas are also applicable to it. Before all, it is important to grasp the resemblance of the two cases, and their difference.

Lord Kelvin has striven to determine in this manner the dimensions of the milky way; for that we are reduced to counting the stars visible in our telescopes; but we are not sure that behind the stars we see, there are not others we do not see; so that what we should measure in this way would not be the size of the milky way, it would be the range of our instruments.

The new theory comes to offer us other resources. In fact, we know the motions of the stars nearest us, and we can form an idea of the rapidity and direction of their velocities. If the ideas above set forth are exact, these velocities should follow Maxwell’s law, and their mean value will tell us, so to speak, that which corresponds to the temperature of our fictitious gas. But this temperature depends itself upon the dimensions of our gas bubble. In fact, how will a gaseous mass let loose in the void act, if its elements attract one another according to Newton’s law? It will take a spherical form; moreover, because of gravitation, the density will be greater at the center, the pressure also will increase from the surface to the center because of the weight of the outer parts drawn toward the center; finally, the temperature will increase toward the center: the temperature and the pressure being connected by the law called adiabatic, as happens in the successive layers of our atmosphere. At the surface itself, the pressure will be null, and it will be the same with the absolute temperature, that is to say with the velocity of the molecules.

A question comes here: I have spoken of the adiabatic law, but this law is not the same for all gases, since it depends upon the ratio of their two specific heats; for the air and like gases, this ratio is 1.42; but is it to air that it is proper to liken the milky way? Evidently not, it should be regarded as a mono-atomic gas, like mercury vapor, like argon, like helium, that is to say that the ratio of the specific heats should be taken equal to 1.66. And, in fact, one of our molecules would be for example the solar system; but the planets are very small personages, the sun alone counts, so that our molecule is indeed mono-atomic. And even if we take a double star, it is probable that the action of a strange star which might approach it would become sufficiently sensible to deviate the motion of general translation of the system much before being able to trouble the relative orbits of the two components; the double star, in a word, would act like an indivisible atom.

However that may be, the pressure, and consequently the temperature, at the center of the gaseous sphere would be by so much the greater as the sphere was larger since the pressure increases by the weight of all the superposed layers. We may suppose that we are nearly at the center of the milky way, and by observing the mean proper velocity of the stars, we shall know that which corresponds to the central temperature of our gaseous sphere and we shall determine its radius.

We may get an idea of the result by the following considerations: make a simpler hypothesis: the milky way is
spherical, and in it the masses are distributed in a homogeneous manner; thence results that the stars in it describe
ellipses having the same center. If we suppose the velocity becomes nothing at the surface, we may calculate this
velocity at the center by the equation of vis viva. Thus we find that this velocity is proportional to the radius of
the sphere and to the square root of its density. If the mass of this sphere was that of the sun and its radius that of
the terrestrial orbit, this velocity would be (it is easy to see) that of the earth in its orbit. But in the case we
have supposed, the mass of the sun should be distributed in a sphere of radius 1,000,000 times greater, this radius
being the distance of the nearest stars; the density is therefore 10^{18} times less; now, the velocities are
of the same order, therefore it is necessary that the radius be 10^{9} times greater, be 1,000 times the
distance of the nearest stars, which would give about a thousand millions of stars in the milky way.

But you will say these hypothesis differ greatly from the reality; first, the milky way is not spherical and we shall soon return to this point, and again the kinetic theory of gases is not compatible with the hypothesis of a homogeneous sphere. But in making the exact calculation according to this theory, we should find a different result, doubtless, but of the same order of magnitude; now in such a problem the data are so uncertain that the order of magnitude is the sole end to be aimed at.

And here a first remark presents itself; Lord Kelvin’s result, which I have obtained again by an approximative calculation, agrees sensibly with the evaluations the observers have made with their telescopes; so that we must conclude we are very near to piercing through the milky way. But that enables us to answer another question. There are the stars we see because they shine; but may there not be dark stars circulating in the interstellar spaces whose existence might long remain unknown? But then, what Lord Kelvin’s method would give us would be the total number of stars, including the dark stars; as his figure is comparable to that the telescope gives, this means there is no dark matter, or at least not so much as of shining matter.

Before going further, we must look at the problem from another angle. Is the milky way thus constituted truly the
image of a gas properly so called? You know Crookes has introduced the notion of a fourth state of matter, where gases
having become too rarefied are no longer true gases and become what he calls radiant matter. Considering the slight
density of the milky way, is it the image of gaseous matter or of radiant matter? The consideration of what is called
the *free path* will furnish us the answer.

The trajectory of a gaseous molecule may be regarded as formed of straight segments united by very small arcs
corresponding to the successive impacts. The length of each of these segments is what is called the free path; of
course this length is not the same for all the segments and for all the molecules; but we may take a mean; this is what
is called the *mean path*. This is the greater the less the density of the gas. The matter will be radiant if
the mean path is greater than the dimensions of the receptacle wherein the gas is enclosed, so that a molecule has a
chance to go across the whole receptacle without undergoing an impact; if the contrary be the case, it is gaseous. From
this it follows that the same fluid may be radiant in a little receptacle and gaseous in a big one; this perhaps is
why, in a Crookes tube, it is necessary to make the vacuum by so much the more complete as the tube is larger.

How is it then for the milky way? This is a mass of gas of which the density is very slight, but whose dimensions
are very great; has a star chances of traversing it without undergoing an impact, that is to say without passing
sufficiently near another star to be sensibly deviated from its route! What do we mean by
*sufficiently near*? That is perforce a little arbitrary; take it as the distance from the sun to Neptune, which
would represent a deviation of a dozen degrees; suppose therefore each of our stars surrounded by a protective sphere
of this radius; could a straight pass between these spheres? At the mean distance of the stars of the milky way, the
radius of these spheres will be seen under an angle of about a tenth of a second; and we have a thousand millions of
stars. Put upon the celestial sphere a thousand million little circles of a tenth of a second radius. Are the chances
that these circles will cover a great number of times the celestial sphere? Far from it; they will cover only its
sixteen thousandth part. So the milky way is not the image of gaseous matter, but of Crookes’ radiant matter.
Nevertheless, as our foregoing conclusions are happily not at all precise, we need not sensibly modify them.

But there is another difficulty: the milky way is not spherical, and we have reasoned hitherto as if it were, since this is the form of equilibrium a gas isolated in space would take. To make amends, agglomerations of stars exist whose form is globular and to which would better apply what we have hitherto said. Herschel has already endeavored to explain their remarkable appearances. He supposed the stars of the aggregates uniformly distributed, so that an assemblage is a homogeneous sphere; each star would then describe an ellipse and all these orbits would be passed over in the same time, so that at the end of a period the aggregate would take again its primitive configuration and this configuration would be stable. Unluckily, the aggregates do not appear to be homogeneous; we see a condensation at the center, we should observe it even were the sphere homogeneous, since it is thicker at the center; but it would not be so accentuated. We may therefore rather compare an aggregate to a gas in adiabatic equilibrium, which takes the spherical form because this is the figure of equilibrium of a gaseous mass.

But, you will say, these aggregates are much smaller than the milky way, of which they even in probability make part, and even though they be more dense, they will rather present something analogous to radiant matter; now, gases attain their adiabatic equilibrium only through innumerable impacts of the molecules. That might perhaps be adjusted. Suppose the stars of the aggregate have just enough energy for their velocity to become null when they reach the surface; then they may traverse the aggregate without impact, but arrived at the surface they will go back and will traverse it anew; after a great number of crossings, they will at last be deviated by an impact; under these conditions, we should still have a matter which might be regarded as gaseous; if perchance there had been in the aggregate stars whose velocity was greater, they have long gone away out of it, they have left it never to return. For all these reasons, it would be interesting to examine the known aggregates, to seek to account for the law of the densities, and to see if it is the adiabatic law of gases.

But to return to the milky way; it is not spherical and would rather be represented as a flattened disc. It is clear then that a mass starting without velocity from the surface will reach the center with different velocities, according as it starts from the surface in the neighborhood of the middle of the disc or just on the border of the disc; the velocity would be notably greater in the latter case. Now, up to the present, we have supposed that the proper velocities of the stars, those we observe, must be comparable to those which like masses would attain; this involves a certain difficulty. We have given above a value for the dimensions of the milky way, and we have deduced it from the observed proper velocities which are of the same order of magnitude as that of the earth in its orbit; but which is the dimension we have thus measured? Is it the thickness? Is it the radius of the disc? It is doubtless something intermediate; but what can we say then of the thickness itself, or of the radius of the disc? Data are lacking to make the calculation; I shall confine myself to giving a glimpse of the possibility of basing an evaluation at least approximate upon a deeper discussion of the proper motions.

And then we find ourselves facing two hypotheses: either the stars of the milky way are impelled by velocities for the most part parallel to the galactic plane, but otherwise distributed uniformly in all directions parallel to this plane. If this be so, observation of the proper motions should show a preponderance of components parallel to the milky way; this is to be determined, because I do not know whether a systematic discussion has ever been made from this view-point. On the other hand, such an equilibrium could only be provisory, since because of impacts the molecules, I mean the stars, would in the long run acquire notable velocities in the sense perpendicular to the milky way and would end by swerving from its plane, so that the system would tend toward the spherical form, the only figure of equilibrium of an isolated gaseous mass.

Or else the whole system is impelled by a common rotation, and for that reason is flattened like the earth, like
Jupiter, like all bodies that twirl. Only, as the flattening is considerable, the rotation must be rapid; rapid
doubtless, but it must be understood in what sense this word is used. The density of the milky way is 10^{23}
times less than that of the sun; a velocity of rotation √10^{25} times less than that of the sun, for it would,
therefore, be the equivalent so far as concerns flattening; a velocity 10^{12} times slower than that of the
earth, say a thirtieth of a second of arc in a century, would be a very rapid rotation, almost too rapid for stable
equilibrium to be possible.

In this hypothesis, the observable proper motions would appear to us uniformly distributed, and there would no longer be a preponderance of components parallel to the galactic plane.

They will tell us nothing about the rotation itself, since we belong to the turning system. If the spiral nebulæ are other milky ways, foreign to ours, they are not borne along in this rotation, and we might study their proper motions. It is true they are very far away; if a nebula has the dimensions of the milky way and if its apparent radius is for example 20´´, its distance is 10,000 times the radius of the milky way.

But that makes no difference, since it is not about the translation of our system that we ask information from them, but about its rotation. The fixed stars, by their apparent motion, reveal to us the diurnal rotation of the earth, though their distance is immense. Unluckily, the possible rotation of the milky way, however rapid it may be relatively, is very slow viewed absolutely, and besides the pointings on nebulæ can not be very precise; therefore thousands of years of observations would be necessary to learn anything.

However that may be, in this second hypothesis, the figure of the milky way would be a figure of final equilibrium.

I shall not further discuss the relative value of these two hypotheses since there is a third which is perhaps more probable. We know that among the irresolvable nebulæ, several kinds may be distinguished: the irregular nebulæ like that of Orion, the planetary and annular nebulæ, the spiral nebulæ. The spectra of the first two families have been determined, they are discontinuous; these nebulæ are therefore not formed of stars; besides, their distribution on the heavens seems to depend upon the milky way; whether they have a tendency to go away from it, or on the contrary to approach it, they make therefore a part of the system. On the other hand, the spiral nebulæ are generally considered as independent of the milky way; it is supposed that they, like it, are formed of a multitude of stars, that they are, in a word, other milky ways very far away from ours. The recent investigations of Stratonoff tend to make us regard the milky way itself as a spiral nebula, and this is the third hypothesis of which I wish to speak.

How can we explain the very singular appearances presented by the spiral nebulæ, which are too regular and too
constant to be due to chance? First of all, to take a look at one of these representations is enough to see that the
mass is in rotation; we may even see what the sense of the rotation is; all the spiral radii are curved in the same
sense; it is evident that the *moving wing* lags behind the pivot and that fixes the sense of the rotation. But
this is not all; it is evident that these nebulæ can not be likened to a gas at rest, nor even to a gas in relative
equilibrium under the sway of a uniform rotation; they are to be compared to a gas in permanent motion in which
internal currents prevail.

Suppose, for example, that the rotation of the central nucleus is rapid (you know what I mean by this word), too rapid for stable equilibrium; then at the equator the centrifugal force will drive it away over the attraction, and the stars will tend to break away at the equator and will form divergent currents; but in going away, as their moment of rotation remains constant, while the radius vector augments, their angular velocity will diminish, and this is why the moving wing seems to lag back.

From this point of view, there would not be a real permanent motion, the central nucleus would constantly lose matter which would go out of it never to return, and would drain away progressively. But we may modify the hypothesis. In proportion as it goes away, the star loses its velocity and ends by stopping; at this moment attraction regains possession of it and leads it back toward the nucleus; so there will be centripetal currents. We must suppose the centripetal currents are the first rank and the centrifugal currents the second rank, if we adopt the comparison with a troop in battle executing a change of front; and, in fact, it is necessary that the composite centrifugal force be compensated by the attraction exercised by the central layers of the swarm upon the extreme layers.

Besides, at the end of a certain time a permanent régime establishes itself; the swarm being curved, the attraction exercised upon the pivot by the moving wing tends to slow up the pivot and that of the pivot upon the moving wing tends to accelerate the advance of this wing which no longer augments its lag, so that finally all the radii end by turning with a uniform velocity. We may still suppose that the rotation of the nucleus is quicker than that of the radii.

A question remains; why do these centripetal and centrifugal swarms tend to concentrate themselves in radii instead of disseminating themselves a little everywhere? Why do these rays distribute themselves regularly? If the swarms concentrate themselves, it is because of the attraction exercised by the already existing swarms upon the stars which go out from the nucleus in their neighborhood. After an inequality is produced, it tends to accentuate itself in this way.

Why do the rays distribute themselves regularly? That is less obvious. Suppose there is no rotation, that all the stars are in two planes at right angles, in such a way that their distribution is symmetric with regard to these two planes.

By symmetry, there would be no reason for their going out of these planes, nor for the symmetry changing. This
configuration would give us therefore equilibrium, but *this would be an unstable equilibrium*.

If on the contrary, there is rotation, we shall find an analogous configuration of equilibrium with four curved rays, equal to each other and intersecting at 90°, and if the rotation is sufficiently rapid, this equilibrium is stable.

I am not in position to make this more precise: enough if you see that these spiral forms may perhaps some day be explained by only the law of gravitation and statistical consideration recalling those of the theory of gases.

What has been said of internal currents shows it is of interest to discuss systematically the aggregate of proper motions; this may be done in a hundred years, when the second edition is issued of the chart of the heavens and compared with the first, that we now are making.

But, in conclusion, I wish to call your attention to a question, that of the age of the milky way or the nebulæ. If what we think we see is confirmed, we can get an idea of it. That sort of statistical equilibrium of which gases give us the model is established only in consequence of a great number of impacts. If these impacts are rare, it can come about only after a very long time; if really the milky way (or at least the agglomerations which are contained in it), if the nebulæ have attained this equilibrium, this means they are very old, and we shall have an inferior limit of their age. Likewise we should have of it a superior limit; this equilibrium is not final and can not last always. Our spiral nebulæ would be comparable to gases impelled by permanent motions; but gases in motion are viscous and their velocities end by wearing out. What here corresponds to the viscosity (and which depends upon the chances of impact of the molecules) is excessively slight, so that the present régime may persist during an extremely long time, yet not forever, so that our milky ways can not live eternally nor become infinitely old.

And this is not all. Consider our atmosphere: at the surface must reign a temperature infinitely small and the velocity of the molecules there is near zero. But this is a question only of the mean velocity; as a consequence of impacts, one of these molecules may acquire (rarely, it is true) an enormous velocity, and then it will rush out of the atmosphere, and once out, it will never return; therefore our atmosphere drains off thus with extreme slowness. The milky way also from time to time loses a star by the same mechanism, and that likewise limits its duration.

Well, it is certain that if we compute in this manner the age of the milky way, we shall get enormous figures. But here a difficulty presents itself. Certain physicists, relying upon other considerations, reckon that suns can have only an ephemeral existence, about fifty million years; our minimum would be much greater than that. Must we believe that the evolution of the milky way began when the matter was still dark? But how have the stars composing it reached all at the same time adult age, an age so briefly to endure? Or must they reach there all successively, and are those we see only a feeble minority compared with those extinguished or which shall one day light up? But how reconcile that with what we have said above on the absence of a noteworthy proportion of dark matter? Should we abandon one of the two hypotheses, and which? I confine myself to pointing out the difficulty without pretending to solve it; I shall end therefore with a big interrogation point.

However, it is interesting to set problems, even when their solution seems very far away.

Every one understands our interest in knowing the form and dimensions of our earth; but some persons will perhaps be surprised at the exactitude sought after. Is this a useless luxury? What good are the efforts so expended by the geodesist?

Should this question be put to a congressman, I suppose he would say: “I am led to believe that geodesy is one of the most useful of the sciences; because it is one of those costing us most dear.” I shall try to give you an answer a little more precise.

The great works of art, those of peace as well as those of war, are not to be undertaken without long studies which save much groping, miscalculation and useless expense. These studies can only be based upon a good map. But a map will be only a valueless phantasy if constructed without basing it upon a solid framework. As well make stand a human body minus the skeleton.

Now, this framework is given us by geodesic measurements; so, without geodesy, no good map; without a good map, no great public works.

These reasons will doubtless suffice to justify much expense; but these are arguments for practical men. It is not upon these that it is proper to insist here; there are others higher and, everything considered, more important.

So we shall put the question otherwise; can geodesy aid us the better to know nature? Does it make us understand its unity and harmony? In reality an isolated fact is of slight value, and the conquests of science are precious only if they prepare for new conquests.

If therefore a little hump were discovered on the terrestrial ellipsoid, this discovery would be by itself of no great interest. On the other hand, it would become precious if, in seeking the cause of this hump, we hoped to penetrate new secrets.

Well, when, in the eighteenth century, Maupertuis and La Condamine braved such opposite climates, it was not solely to learn the shape of our planet, it was a question of the whole world-system.

If the earth was flattened, Newton triumphed and with him the doctrine of gravitation and the whole modern celestial mechanics.

And to-day, a century and a half after the victory of the Newtonians, think you geodesy has nothing more to teach us?

We know not what is within our globe. The shafts of mines and borings have let us know a layer of 1 or 2 kilometers thickness, that is to say, the millionth part of the total mass; but what is beneath?

Of all the extraordinary journeys dreamed by Jules Verne, perhaps that to the center of the earth took us to regions least explored.

But these deep-lying rocks we can not reach, exercise from afar their attraction which operates upon the pendulum and deforms the terrestrial spheroid. Geodesy can therefore weigh them from afar, so to speak, and tell us of their distribution. Thus will it make us really see those mysterious regions which Jules Verne only showed us in imagination.

This is not an empty illusion. M. Faye, comparing all the measurements, has reached a result well calculated to surprise us. Under the oceans, in the depths, are rocks of very great density; under the continents, on the contrary, are empty spaces.

New observations will modify perhaps the details of these conclusions.

In any case, our venerated dean has shown us where to search and what the geodesist may teach the geologist, desirous of knowing the interior constitution of the earth, and even the thinker wishing to speculate upon the past and the origin of this planet.

And now, why have I entitled this chapter *French Geodesy*? It is because, in each country, this science has
taken, more than all others, perhaps, a national character. It is easy to see why.

There must be rivalry. The scientific rivalries are always courteous, or at least almost always; in any case, they are necessary, because they are always fruitful. Well, in those enterprises which require such long efforts and so many collaborators, the individual is effaced, in spite of himself, of course; no one has the right to say: this is my work. Therefore it is not between men, but between nations that rivalries go on.

So we are led to seek what has been the part of France. Her part I believe we are right to be proud of.

At the beginning of the eighteenth century, long discussions arose between the Newtonians who believed the earth flattened, as the theory of gravitation requires, and Cassini, who, deceived by inexact measurements, believed our globe elongated. Only direct observation could settle the question. It was our Academy of Sciences that undertook this task, gigantic for the epoch.

While Maupertuis and Clairaut measured a degree of meridian under the polar circle, Bouguer and La Condamine went toward the Andes Mountains, in regions then under Spain which to-day are the Republic of Ecuador.

Our envoys were exposed to great hardships. Traveling was not as easy as at present.

Truly, the country where Maupertuis operated was not a desert and he even enjoyed, it is said, among the Laplanders those sweet satisfactions of the heart that real arctic voyagers never know. It was almost the region where, in our days, comfortable steamers carry, each summer, hosts of tourists and young English people. But in those days Cook’s agency did not exist and Maupertuis really believed he had made a polar expedition.

Perhaps he was not altogether wrong. The Russians and the Swedes carry out to-day analogous measurements at Spitzbergen, in a country where there is real ice-cap. But they have quite other resources, and the difference of time makes up for that of latitude.

The name of Maupertuis has reached us much scratched by the claws of Doctor Akakia; the scientist had the misfortune to displease Voltaire, who was then the king of mind. He was first praised beyond measure; but the flatteries of kings are as much to be dreaded as their displeasure, because the days after are terrible. Voltaire himself knew something of this.

Voltaire called Maupertuis, my amiable master in thinking, marquis of the polar circle, dear flattener out of the world and Cassini, and even, flattery supreme, Sir Isaac Maupertuis; he wrote him: “Only the king of Prussia do I put on a level with you; he only lacks being a geometer.” But soon the scene changes, he no longer speaks of deifying him, as in days of yore the Argonauts, or of calling down from Olympus the council of the gods to contemplate his works, but of chaining him up in a madhouse. He speaks no longer of his sublime mind, but of his despotic pride, plated with very little science and much absurdity.

I care not to relate these comico-heroic combats; but permit me some reflections on two of Voltaire’s verses. In his ‘Discourse on Moderation’ (no question of moderation in praise and criticism), the poet has written:

You have confirmed in regions drear

What Newton discerned without going abroad.

These two verses (which replace the hyperbolic praises of the first period) are very unjust, and doubtless Voltaire was too enlightened not to know it.

Then, only those discoveries were esteemed which could be made without leaving one’s house.

To-day, it would rather be theory that one would make light of.

This is to misunderstand the aim of science.

Is nature governed by caprice, or does harmony rule there? That is the question. It is when it discloses to us this harmony that science is beautiful and so worthy to be cultivated. But whence can come to us this revelation, if not from the accord of a theory with experiment? To seek whether this accord exists or if it fails, this therefore is our aim. Consequently these two terms, which we must compare, are as indispensable the one as the other. To neglect one for the other would be nonsense. Isolated, theory would be empty, experiment would be blind; each would be useless and without interest.

Maupertuis therefore deserves his share of glory. Truly, it will not equal that of Newton, who had received the spark divine; nor even that of his collaborator Clairaut. Yet it is not to be despised, because his work was necessary, and if France, outstripped by England in the seventeenth century, has so well taken her revenge in the century following, it is not alone to the genius of Clairauts, d’Alemberts, Laplaces that she owes it; it is also to the long patience of the Maupertuis and the La Condamines.

We reach what may be called the second heroic period of geodesy. France is torn within. All Europe is armed against her; it would seem that these gigantic combats might absorb all her forces. Far from it; she still has them for the service of science. The men of that time recoiled before no enterprise, they were men of faith.

Delambre and Méchain were commissioned to measure an arc going from Dunkerque to Barcelona. This time there was no going to Lapland or to Peru; the hostile squadrons had closed to us the ways thither. But, though the expeditions are less distant, the epoch is so troubled that the obstacles, the perils even, are just as great.

In France, Delambre had to fight against the ill-will of suspicious municipalities. One knows that the steeples, which are visible from so far, and can be aimed at with precision, often serve as signal points to geodesists. But in the region Delambre traversed there were no longer any steeples. A certain proconsul had passed there, and boasted of knocking down all the steeples rising proudly above the humble abode of the sans-culottes. Pyramids then were built of planks and covered with white cloth to make them more visible. That was quite another thing: with white cloth! What was this rash person who, upon our heights so recently set free, dared to raise the hateful standard of the counter-revolution? It was necessary to border the white cloth with blue and red bands.

Méchain operated in Spain; the difficulties were other; but they were not less. The Spanish peasants were hostile. There steeples were not lacking: but to install oneself in them with mysterious and perhaps diabolic instruments, was it not sacrilege? The revolutionists were allies of Spain, but allies smelling a little of the stake.

“Without cease,” writes Méchain, “they threaten to butcher us.” Fortunately, thanks to the exhortations of the priests, to the pastoral letters of the bishops, these ferocious Spaniards contented themselves with threatening.

Some years after Méchain made a second expedition into Spain: he proposed to prolong the meridian from Barcelona to the Balearics. This was the first time it had been attempted to make the triangulations overpass a large arm of the sea by observing signals installed upon some high mountain of a far-away isle. The enterprise was well conceived and well prepared; it failed however.

The French scientist encountered all sorts of difficulties of which he complains bitterly in his correspondence. “Hell,” he writes, perhaps with some exaggeration —“hell and all the scourges it vomits upon the earth, tempests, war, the plague and black intrigues are therefore unchained against me!”

The fact is that he encountered among his collaborators more of proud obstinacy than of good will and that a thousand accidents retarded his work. The plague was nothing, the fear of the plague was much more redoubtable; all these isles were on their guard against the neighboring isles and feared lest they should receive the scourge from them. Méchain obtained permission to disembark only after long weeks upon the condition of covering all his papers with vinegar; this was the antisepsis of that time.

Disgusted and sick, he had just asked to be recalled, when he died.

Arago and Biot it was who had the honor of taking up the unfinished work and carrying it on to completion.

Thanks to the support of the Spanish government, to the protection of several bishops and, above all, to that of a famous brigand chief, the operations went rapidly forward. They were successfully completed, and Biot had returned to France when the storm burst.

It was the moment when all Spain took up arms to defend her independence against France. Why did this stranger climb the mountains to make signals? It was evidently to call the French army. Arago was able to escape the populace only by becoming a prisoner. In his prison, his only distraction was reading in the Spanish papers the account of his own execution. The papers of that time sometimes gave out news prematurely. He had at least the consolation of learning that he died with courage and like a Christian.

Even the prison was no longer safe; he had to escape and reach Algiers. There, he embarked for Marseilles on an Algerian vessel. This ship was captured by a Spanish corsair, and behold Arago carried back to Spain and dragged from dungeon to dungeon, in the midst of vermin and in the most shocking wretchedness.

If it had only been a question of his subjects and his guests, the dey would have said nothing. But there were on board two lions, a present from the African sovereign to Napoleon. The dey threatened war.

The vessel and the prisoners were released. The port should have been properly reached, since they had on board an astronomer; but the astronomer was seasick, and the Algerian seamen, who wished to make Marseilles, came out at Bougie. Thence Arago went to Algiers, traversing Kabylia on foot in the midst of a thousand perils. He was long detained in Africa and threatened with the convict prison. Finally he was able to get back to France; his observations, which he had preserved and safeguarded under his shirt, and, what is still more remarkable, his instruments had traversed unhurt these terrible adventures. Up to this point, not only did France hold the foremost place, but she occupied the stage almost alone.

In the years which follow, she has not been inactive and our staff-office map is a model. However, the new methods of observation and calculation have come to us above all from Germany and England. It is only in the last forty years that France has regained her rank. She owes it to a scientific officer, General Perrier, who has successfully executed an enterprise truly audacious, the junction of Spain and Africa. Stations were installed on four peaks upon the two sides of the Mediterranean. For long months they awaited a calm and limpid atmosphere. At last was seen the little thread of light which had traversed 300 kilometers over the sea. The undertaking had succeeded.

To-day have been conceived projects still more bold. From a mountain near Nice will be sent signals to Corsica, not now for geodesic determinations, but to measure the velocity of light. The distance is only 200 kilometers; but the ray of light is to make the journey there and return, after reflection by a mirror installed in Corsica. And it should not wander on the way, for it must return exactly to the point of departure.

Ever since, the activity of French geodesy has never slackened. We have no more such astonishing adventures to tell; but the scientific work accomplished is immense. The territory of France beyond the sea, like that of the mother country, is covered by triangles measured with precision.

We have become more and more exacting and what our fathers admired does not satisfy us to-day. But in proportion as we seek more exactitude, the difficulties greatly increase; we are surrounded by snares and must be on our guard against a thousand unsuspected causes of error. It is needful, therefore, to create instruments more and more faultless.

Here again France has not let herself be distanced. Our appliances for the measurement of bases and angles leave nothing to desire, and, I may also mention the pendulum of Colonel Defforges, which enables us to determine gravity with a precision hitherto unknown.

The future of French geodesy is at present in the hands of the Geographic Service of the army, successively directed by General Bassot and General Berthaut. We can not sufficiently congratulate ourselves upon it. For success in geodesy, scientific aptitudes are not enough; it is necessary to be capable of standing long fatigues in all sorts of climates; the chief must be able to win obedience from his collaborators and to make obedient his native auxiliaries. These are military qualities. Besides, one knows that, in our army, science has always marched shoulder to shoulder with courage.

I add that a military organization assures the indispensable unity of action. It would be more difficult to reconcile the rival pretensions of scientists jealous of their independence, solicitous of what they call their fame, and who yet must work in concert, though separated by great distances. Among the geodesists of former times there were often discussions, of which some aroused long echoes. The Academy long resounded with the quarrel of Bouguer and La Condamine. I do not mean to say that soldiers are exempt from passion, but discipline imposes silence upon a too sensitive self-esteem.

Several foreign governments have called upon our officers to organize their geodesic service: this is proof that the scientific influence of France abroad has not declined.

Our hydrographic engineers contribute also to the common achievement a glorious contingent. The survey of our coasts, of our colonies, the study of the tides, offer them a vast domain of research. Finally I may mention the general leveling of France which is carried out by the ingenious and precise methods of M. Lallemand.

With such men we are sure of the future. Moreover, work for them will not be lacking; our colonial empire opens for them immense expanses illy explored. That is not all: the International Geodetic Association has recognized the necessity of a new measurement of the arc of Quito, determined in days of yore by La Condamine. It is France that has been charged with this operation; she had every right to it, since our ancestors had made, so to speak, the scientific conquest of the Cordilleras. Besides, these rights have not been contested and our government has undertaken to exercise them.

Captains Maurain and Lacombe completed a first reconnaissance, and the rapidity with which they accomplished their mission, crossing the roughest regions and climbing the most precipitous summits, is worthy of all praise. It won the admiration of General Alfaro, President of the Republic of Ecuador, who called them ‘los hombres de hierro,’ the men of iron.

The final commission then set out under the command of Lieutenant-Colonel (then Major) Bourgeois. The results obtained have justified the hopes entertained. But our officers have encountered unforeseen difficulties due to the climate. More than once, one of them has been forced to remain several months at an altitude of 4,000 meters, in the clouds and the snow, without seeing anything of the signals he had to aim at and which refused to unmask themselves. But thanks to their perseverance and courage, there resulted from this only a delay and an increase of expense, without the exactitude of the measurements suffering therefrom.

What I have sought to explain in the preceding pages is how the scientist should guide himself in choosing among the innumerable facts offered to his curiosity, since indeed the natural limitations of his mind compel him to make a choice, even though a choice be always a sacrifice. I have expounded it first by general considerations, recalling on the one hand the nature of the problem to be solved and on the other hand seeking to better comprehend that of the human mind, which is the principal instrument of the solution. I then have explained it by examples; I have not multiplied them indefinitely; I also have had to make a choice, and I have chosen naturally the questions I had studied most. Others would doubtless have made a different choice; but what difference, because I believe they would have reached the same conclusions.

There is a hierarchy of facts; some have no reach; they teach us nothing but themselves. The scientist who has ascertained them has learned nothing but a fact, and has not become more capable of foreseeing new facts. Such facts, it seems, come once, but are not destined to reappear.

There are, on the other hand, facts of great yield; each of them teaches us a new law. And since a choice must be made, it is to these that the scientist should devote himself.

Doubtless this classification is relative and depends upon the weakness of our mind. The facts of slight outcome are the complex facts, upon which various circumstances may exercise a sensible influence, circumstances too numerous and too diverse for us to discern them all. But I should rather say that these are the facts we think complex, since the intricacy of these circumstances surpasses the range of our mind. Doubtless a mind vaster and finer than ours would think differently of them. But what matter; we can not use that superior mind, but only our own.

The facts of great outcome are those we think simple; may be they really are so, because they are influenced only by a small number of well-defined circumstances, may be they take on an appearance of simplicity because the various circumstances upon which they depend obey the laws of chance and so come to mutually compensate. And this is what happens most often. And so we have been obliged to examine somewhat more closely what chance is.

Facts where the laws of chance apply become easy of access to the scientist who would be discouraged before the extraordinary complication of the problems where these laws are not applicable. We have seen that these considerations apply not only to the physical sciences, but to the mathematical sciences. The method of demonstration is not the same for the physicist and the mathematician. But the methods of invention are very much alike. In both cases they consist in passing up from the fact to the law, and in finding the facts capable of leading to a law.

To bring out this point, I have shown the mind of the mathematician at work, and under three forms: the mind of the mathematical inventor and creator; that of the unconscious geometer who among our far distant ancestors, or in the misty years of our infancy, has constructed for us our instinctive notion of space; that of the adolescent to whom the teachers of secondary education unveil the first principles of the science, seeking to give understanding of the fundamental definitions. Everywhere we have seen the rôle of intuition and of the spirit of generalization without which these three stages of mathematicians, if I may so express myself, would be reduced to an equal impotence.

And in the demonstration itself, the logic is not all; the true mathematical reasoning is a veritable induction, different in many regards from the induction of physics, but proceeding like it from the particular to the general. All the efforts that have been made to reverse this order and to carry back mathematical induction to the rules of logic have eventuated only in failures, illy concealed by the employment of a language inaccessible to the uninitiated. The examples I have taken from the physical sciences have shown us very different cases of facts of great outcome. An experiment of Kaufmann on radium rays revolutionizes at the same time mechanics, optics and astronomy. Why? Because in proportion as these sciences have developed, we have the better recognized the bonds uniting them, and then we have perceived a species of general design of the chart of universal science. There are facts common to several sciences, which seem the common source of streams diverging in all directions and which are comparable to that knoll of Saint Gothard whence spring waters which fertilize four different valleys.

And then we can make choice of facts with more discernment than our predecessors who regarded these valleys as distinct and separated by impassable barriers.

It is always simple facts which must be chosen, but among these simple facts we must prefer those which are situated upon these sorts of knolls of Saint Gothard of which I have just spoken.

And when sciences have no direct bond, they still mutually throw light upon one another by analogy. When we studied the laws obeyed by gases we knew we had attacked a fact of great outcome; and yet this outcome was still estimated beneath its value, since gases are, from a certain point of view, the image of the milky way, and those facts which seemed of interest only for the physicist, ere long opened new vistas to astronomy quite unexpected.

And finally when the geodesist sees it is necessary to move his telescope some seconds to see a signal he has set up with great pains, this is a very small fact; but this is a fact of great outcome, not only because this reveals to him the existence of a small protuberance upon the terrestrial globe, that little hump would be by itself of no great interest, but because this protuberance gives him information about the distribution of matter in the interior of the globe, and through that about the past of our planet, about its future, about the laws of its development.

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