CHAPTER XXI.

THEORY OF APPROXIMATION.

In order that we may gain a true understanding of the kind, degree, and value of the knowledge which we acquire by experimental investigation, it is requisite that we should be fully conscious of its approximate character. We must learn to distinguish between what we can know and cannot know--between the questions which admit of solution, and those which only seem to be solved. Many persons may be misled by the expression *exact science*, and may think that the knowledge acquired by scientific methods admits of our reaching absolutely true laws, exact to the last degree. There is even a prevailing impression that when once mathematical formulæ have been successfully applied to a branch of science, this portion of knowledge assumes a new nature, and admits of reasoning of a higher character than those sciences which are still unmathematical.

The very satisfactory degree of accuracy attained in the science of astronomy gives a certain plausibility to erroneous notions of this kind. Some persons no doubt consider it to be *proved* that planets move in ellipses, in such a manner that all Kepler’s laws hold exactly true; but there is a double error in any such notions. In the first place, Kepler’s laws are *not proved*, if by proof we mean certain demonstration of their exact truth. In the next place, even assuming Kepler’s laws to be exactly true in a theoretical point of view, the planets never move according to those laws. Even if we could observe the motions of a planet, of a perfect globular form, free from all perturbing or retarding forces, we could never prove that it moved in a perfect ellipse. To prove the elliptical form we should have to measure infinitely small angles, and infinitely small fractions of a second; we should have to perform impossibilities. All we can do is to show that the motion of an unperturbed planet approaches *very nearly* to the form of an ellipse, and more nearly the more accurately our observations are made. But if we go on to assert that the path *is* an ellipse we pass beyond our data, and make an assumption which cannot be verified by observation.

But, secondly, as a matter of fact no planet does move in a perfect ellipse, or manifest the truth of Kepler’s laws exactly. The law of gravity prevents its own results from being clearly exhibited, because the mutual perturbations of the planets distort the elliptical paths. Those laws, again, hold exactly true only of infinitely small bodies, and when two great globes, like the sun and Jupiter, attract each other, the law must be modified. The periodic time is then shortened in the ratio of the square root of the number expressing the sun’s mass, to that of the sum of the numbers expressing the masses of the sun and planet, as was shown by Newton.[374] Even at the present day discrepancies exist between the observed dimensions of the planetary orbits and their theoretical magnitudes, after making allowance for all disturbing causes.[375] Nothing is more certain in scientific method than that approximate coincidence alone can be expected. In the measurement of continuous quantity perfect correspondence must be accidental, and should give rise to suspicion rather than to satisfaction.

[374] *Principia*, bk. iii. Prop. 15.

[375] Lockyer’s *Lessons in Elementary Astronomy*, p. 301.

One remarkable result of the approximate character of our observations is that we could never prove the existence of perfectly circular or parabolic movement, even if it existed. The circle is a singular case of the ellipse, for which the eccentricity is zero; it is infinitely improbable that any planet, even if undisturbed by other bodies, would have a circle for its orbit; but if the orbit were a circle we could never prove the entire absence of eccentricity. All that we could do would be to declare the divergence from the circular form to be inappreciable. Delambre was unable to detect the slightest ellipticity in the orbit of Jupiter’s first satellite, but he could only infer that the orbit was *nearly* circular. The parabola is the singular limit between the ellipse and the hyperbola. As there are elliptic and hyperbolic comets, so we might conceive the existence of a parabolic comet. Indeed if an undisturbed comet fell towards the sun from an infinite distance it would move in a parabola; but we could never prove that it so moved.

*Substitution of Simple Hypotheses.*

In truth men never can solve problems fulfilling the complex circumstances of nature. All laws and explanations are in a certain sense hypothetical, and apply exactly to nothing which we can know to exist. In place of the actual objects which we see and feel, the mathematician substitutes imaginary objects, only partially resembling those represented, but so devised that the discrepancies are not of an amount to alter seriously the character of the solution. When we probe the matter to the bottom physical astronomy is as hypothetical as Euclid’s elements. There may exist in nature perfect straight lines, triangles, circles, and other regular geometrical figures; to our science it is a matter of indifference whether they do or do not exist, because in any case they must be beyond our powers of perception. If we submitted a perfect circle to the most rigorous scrutiny, it is impossible that we should discover whether it were perfect or not. Nevertheless in geometry we argue concerning perfect curves, and rectilinear figures, and the conclusions apply to existing objects so far as we can assure ourselves that they agree with the hypothetical conditions of our reasoning. This is in reality all that we can do in the most perfect of the sciences.

Doubtless in astronomy we meet with the nearest approximation to actual conditions. The law of gravity is not a complex one in itself, and we believe it with much probability to be exactly true; but we cannot calculate out in any real case its accurate results. The law asserts that every particle of matter in the universe attracts every other particle, with a force depending on the masses of the particles and their distances. We cannot know the force acting on any particle unless we know the masses and distances and positions of all other particles in the universe. The physical astronomer has made a sweeping assumption, namely, that all the millions of existing systems exert no perturbing effects on our planetary system, that is to say, no effects in the least appreciable. The problem at once becomes hypothetical, because there is little doubt that gravitation between our sun and planets and other systems does exist. Even when they consider the relations of our planetary bodies *inter se*, all their processes are only approximate. In the first place they assume that each of the planets is a perfect ellipsoid, with a smooth surface and a homogeneous interior. That this assumption is untrue every mountain and valley, every sea, every mine affords conclusive evidence. If astronomers are to make their calculations perfect, they must not only take account of the Himalayas and the Andes, but must calculate separately the attraction of every hill, nay, of every ant-hill. So far are they from having considered any local inequality of the surface, that they have not yet decided upon the general form of the earth; it is still a matter of speculation whether or not the earth is an ellipsoid with three unequal axes. If, as is probable, the globe is irregularly compressed in some directions, the calculations of astronomers will have to be repeated and refined, in order that they may approximate to the attractive power of such a body. If we cannot accurately learn the form of our own earth, how can we expect to ascertain that of the moon, the sun, and other planets, in some of which probably are irregularities of greater proportional amount?

In a further way the science of physical astronomy is merely approximate and hypothetical. Given homogeneous ellipsoids acting upon each other according to the law of gravity, the best mathematicians have never and perhaps never will determine exactly the resulting movements. Even when three bodies simultaneously attract each other the complication of effects is so great that only approximate calculations can be made. Astronomers have not even attempted the general problem of the simultaneous attractions of four, five, six, or more bodies; they resolve the general problem into so many different problems of three bodies. The principle upon which the calculations of physical astronomy proceed, is to neglect every quantity which does not seem likely to lead to an effect appreciable in observation, and the quantities rejected are far more numerous and complex than the few larger terms which are retained. All then is merely approximate.

Concerning other branches of physical science the same statements are even more evidently true. We speak and calculate about inflexible bars, inextensible lines, heavy points, homogeneous substances, uniform spheres, perfect fluids and gases, and we deduce a great number of beautiful theorems; but all is hypothetical. There is no such thing as an inflexible bar, an inextensible line, nor any one of the other perfect objects of mechanical science; they are to be classed with those mythical existences, the straight line, triangle, circle, &c., about which Euclid so freely reasoned. Take the simplest operation considered in statics--the use of a crowbar in raising a heavy stone, and we shall find, as Thomson and Tait have pointed out, that we neglect far more than we observe.[376] If we suppose the bar to be quite rigid, the fulcrum and stone perfectly hard, and the points of contact real points, we may give the true relation of the forces. But in reality the bar must bend, and the extension and compression of different parts involve us in difficulties. Even if the bar be homogeneous in all its parts, there is no mathematical theory capable of determining with accuracy all that goes on; if, as is infinitely more probable, the bar is not homogeneous, the complete solution will be immensely more complicated, but hardly more hopeless. No sooner had we determined the change of form according to simple mechanical principles, than we should discover the interference of thermodynamic principles. Compression produces heat and extension cold, and thus the conditions of the problem are modified throughout. In attempting a fourth approximation we should have to allow for the conduction of heat from one part of the bar to another. All these effects are utterly inappreciable in a practical point of view, if the bar be a good stout one; but in a theoretical point of view they entirely prevent our saying that we have solved a natural problem. The faculties of the human mind, even when aided by the wonderful powers of abbreviation conferred by analytical methods, are utterly unable to cope with the complications of any real problem. And had we exhausted all the known phenomena of a mechanical problem, how can we tell that hidden phenomena, as yet undetected, do not intervene in the commonest actions? It is plain that no phenomenon comes within the sphere of our senses unless it possesses a momentum capable of irritating the appropriate nerves. There may then be worlds of phenomena too slight to rise within the scope of our consciousness.

[376] *Treatise on Natural Philosophy*, vol. i. pp. 337, &c.

All the instruments with which we perform our measurements are faulty. We assume that a plumb-line gives a vertical line; but this is never true in an absolute sense, owing to the attraction of mountains and other inequalities in the surface of the earth. In an accurate trigonometrical survey, the divergencies of the plumb-line must be approximately determined and allowed for. We assume a surface of mercury to be a perfect plane, but even in the breadth of 5 inches there is a calculable divergence from a true plane of about one ten-millionth part of an inch; and this surface further diverges from true horizontality as the plumb-line does from true verticality. That most perfect instrument, the pendulum, is not theoretically perfect, except for infinitely small arcs of vibration, and the delicate experiments performed with the torsion balance proceed on the assumption that the force of torsion of a wire is proportional to the angle of torsion, which again is only true for infinitely small angles.

Such is the purely approximate character of all our operations that it is not uncommon to find the theoretically worse method giving truer results than the theoretically perfect method. The common pendulum which is not isochronous is better for practical purposes than the cycloidal pendulum, which is isochronous in theory but subject to mechanical difficulties. The spherical form is not the correct form for a speculum or lense, but it differs so slightly from the true form, and is so much more easily produced mechanically, that it is generally best to rest content with the spherical surface. Even in a six-feet mirror the difference between the parabola and the sphere is only about one ten-thousandth part of an inch, a thickness which would be taken off in a few rubs of the polisher. Watts’ ingenious parallel motion was intended to produce rectilinear movement of the piston-rod. In reality the motion was always curvilinear, but for his purposes a certain part of the curve approximated sufficiently to a straight line.

*Approximation to Exact Laws.*

Though we can not prove numerical laws with perfect accuracy, it would be a great mistake to suppose that there is any inexactness in the laws of nature. We may even discover a law which we believe to represent the action of forces with perfect exactness. The mind may seem to pass in advance of its data, and choose out certain numerical results as absolutely true. We can never really pass beyond our data, and so far as assumption enters in, so far want of certainty will attach to our conclusions; nevertheless we may sometimes rightly prefer a probable assumption of a precise law to numerical results, which are at the best only approximate. We must accordingly draw a strong distinction between the laws of nature which we believe to be accurately stated in our formulas, and those to which our statements only make an approximation, so that at a future time the law will be differently stated.

The law of gravitation is expressed in the form F = Mm/D^{2}, meaning that gravity is proportional directly to the product of the gravitating masses, and indirectly to the square of their distance. The latent heat of steam is expressed by the equation log F = *a* + *b*α^{t} + *c*β^{t}, in which are five quantities *a*, *b*, *c*, α, β, to be determined by experiment. There is every reason to believe that in the progress of science the law of gravity will remain entirely unaltered, and the only effect of further inquiry will be to render it a more and more probable expression of the absolute truth. The law of the latent heat of steam on the other hand, will be modified by every new series of experiments, and it may not improbably be shown that the assumed law can never be made to agree exactly with the results of experiment.

Philosophers have not always supposed that the law of gravity was exactly true. Newton, though he had the highest confidence in its truth, admitted that there were motions in the planetary system which he could not reconcile with the law. Euler and Clairaut who were, with D’Alembert, the first to apply the full powers of mathematical analysis to the theory of gravitation as explaining the perturbations of the planets, did not think the law sufficiently established to attribute all discrepancies to the errors of calculation and observation. They did not feel certain that the force of gravity exactly obeyed the well-known rule. The law might involve other powers of the distance. It might be expressed in the form

F = ... + *a*/D + *b*/D^{2} + *c*/D^{3} + ...

and the coefficients *a* and *c* might be so small that those terms would become apparent only in very accurate comparisons with fact. Attempts have been made to account for difficulties, by attributing value to such neglected terms. Gauss at one time thought the even more fundamental principle of gravity, that the force is dependent only on mass and distance, might not be exactly true, and he undertook accurate pendulum experiments to test this opinion. Only as repeated doubts have time after time been resolved in favour of the law of Newton, has it been assumed as precisely correct. But this belief does not rest on experiment or observation only. The calculations of physical astronomy, however accurate, could never show that the other terms of the above expression were absolutely devoid of value. It could only be shown that they had such slight value as never to become apparent.

There are, however, other reasons why the law is probably complete and true as commonly stated. Whatever influence spreads from a point, and expands uniformly through space, will doubtless vary inversely in intensity as the square of the distance, because the area over which it is spread increases as the square of the radius. This part of the law of gravity may be considered as due to the properties of space, and there is a perfect analogy in this respect between gravity and all other *emanating* forces, as was pointed out by Keill.[377] Thus the undulations of light, heat, and sound, and the attractions of electricity and magnetism obey the very same law so far as we can ascertain. If the molecules of a gas or the particles of matter constituting odour were to start from a point and spread uniformly, their distances would increase and their density decrease according to the same principle.

[377] *An Introduction to Natural Philosophy*, 3rd edit. 1733, p. 5.

Other laws of nature stand in a similar position. Dalton’s laws of definite combining proportions never have been, and never can be, exactly proved; but chemists having shown, to a considerable degree of approximation, that the elements combine together as if each element had atoms of an invariable mass, assume that this is exactly true. They go even further. Prout pointed out in 1815 that the equivalent weights of the elements appeared to be simple numbers; and the researches of Dumas, Pelouze, Marignac, Erdmann, Stas, and others have gradually rendered it likely that the atomic weights of hydrogen, carbon, oxygen, nitrogen, chlorine, and silver, are in the ratios of the numbers 1, 12, 16, 14, 35·5, and 108. Chemists then step beyond their data; they throw aside their actual experimental numbers, and assume that the true ratios are not those exactly indicated by any weighings, but the simple ratios of these numbers. They boldly assume that the discrepancies are due to experimental errors, and they are justified by the fact that the more elaborate and skilful the researches on the subject, the more nearly their assumption is verified. Potassium is the only element whose atomic weight has been determined with great care, but which has not shown an approach to a simple ratio with the other elements. This exception may be due to some unsuspected cause of error.[378] A similar assumption is made in the law of definite combining volumes of gases, and Brodie has clearly pointed out the line of argument by which the chemist, observing that the discrepancies between the law and fact are within the limits of experimental error, assumes that they are due to error.[379]

[378] Watts, *Dictionary of Chemistry*, vol. i. p. 455.

[379] *Philosophical Transactions*, (1866) vol. clvi. p. 809.

Faraday, in one of his researches, expressly makes an assumption of the same kind. Having shown, with some degree of experimental precision, that there exists a simple proportion between quantities of electrical energy and the quantities of chemical substances which it can decompose, so that for every atom dissolved in the battery cell an atom ought theoretically, that is without regard to dissipation of some of the energy, to be decomposed in the electrolytic cell, he does not stop at his numerical results. “I have not hesitated,” he says,[380] “to apply the more strict results of chemical analysis to correct the numbers obtained as electrolytic results. This, it is evident, may be done in a great number of cases, without using too much liberty towards the due severity of scientific research.”

[380] *Experimental Researches in Electricity*, vol. i. p. 246.

The law of the conservation of energy, one of the widest of all physical generalisations, rests upon the same footing. The most that we can do by experiment is to show that the energy entering into any experimental combination is almost equal to what comes out of it, and more nearly so the more accurately we perform the measurements. Absolute equality is always a matter of assumption. We cannot even prove the indestructibility of matter; for were an exceedingly minute fraction of existing matter to vanish in any experiment, say one part in ten millions, we could never detect the loss.

*Successive Approximations to Natural Conditions.*

When we examine the history of scientific problems, we find that one man or one generation is usually able to make but a single step at a time. A problem is solved for the first time by making some bold hypothetical simplification, upon which the next investigator makes hypothetical modifications approaching more nearly to the truth. Errors are successively pointed out in previous solutions, until at last there might seem little more to be desired. Careful examination, however, will show that a series of minor inaccuracies remain to be corrected and explained, were our powers of reasoning sufficiently great, and the purpose adequate in importance.

Newton’s successful solution of the problem of the planetary movements entirely depended at first upon a great simplification. The law of gravity only applies directly to two infinitely small particles, so that when we deal with vast globes like the earth, Jupiter, and the sun, we have an immense aggregate of separate attractions to deal with, and the law of the aggregate need not coincide with the law of the elementary particles. But Newton, by a great effort of mathematical reasoning, was able to show that two homogeneous spheres of matter act as if the whole of their masses were concentrated at the centres; in short, that such spheres are centrobaric bodies (p. 364). He was then able with comparative ease to calculate the motions of the planets on the hypothesis of their being spheres, and to show that the results roughly agreed with observation. Newton, indeed, was one of the few men who could make two great steps at once. He did not rest contented with the spherical hypothesis; having reason to believe that the earth was really a spheroid with a protuberance around the equator, he proceeded to a second approximation, and proved that the attraction of the protuberant matter upon the moon accounted for the precession of the equinoxes, and led to various complicated effects. But, (p. 459), even the spheroidal hypothesis is far from the truth. It takes no account of the irregularities of surface, the great protuberance of land in Central Asia and South America, and the deficiency in the bed of the Atlantic.

To determine the law according to which a projectile, such as a cannon ball, moves through the atmosphere is a problem very imperfectly solved at the present day, but in which many successive advances have been made. So little was known concerning the subject three or four centuries ago that a cannon ball was supposed to move at first in a straight line, and after a time to be deflected into a curve. Tartaglia ventured to maintain that the path was curved throughout, as by the principle of continuity it should be; but the ingenuity of Galileo was required to prove this opinion, and to show that the curve was approximately a parabola. It is only, however, under forced hypotheses that we can assert the path of a projectile to be truly a parabola: the path must be through a perfect vacuum, where there is no resisting medium of any kind; the force of gravity must be uniform and act in parallel lines; or else the moving body must be either a mere point, or a perfect centrobaric body, that is a body possessing a definite centre of gravity. These conditions cannot be really fulfilled in practice. The next great step in the problem was made by Newton and Huyghens, the latter of whom asserted that the atmosphere would offer a resistance proportional to the velocity of the moving body, and concluded that the path would have in consequence a logarithmic character. Newton investigated in a general manner the subject of resisting media, and came to the conclusion that the resistance is more nearly proportional to the square of the velocity. The subject then fell into the hands of Daniel Bernoulli, who pointed out the enormous resistance of the air in cases of rapid movement, and calculated that a cannon ball, if fired vertically in a vacuum, would rise eight times as high as in the atmosphere. In recent times an immense amount both of theoretical and experimental investigation has been spent upon the subject, since it is one of importance in the art of war. Successive approximations to the true law have been made, but nothing like a complete and final solution has been achieved or even hoped for.[381]

[381] Hutton’s *Mathematical Dictionary*, vol. ii. pp. 287–292.

It is quite to be expected that the earliest experimenters in any branch of science will overlook errors which afterwards become most apparent. The Arabian astronomers determined the meridian by taking the middle point between the places of the sun when at equal altitudes on the same day. They overlooked the fact that the sun has its own motion in the time between the observations. Newton thought that the mutual disturbances of the planets might be disregarded, excepting perhaps the effect of the mutual attraction of the greater planets, Jupiter and Saturn, near their conjunction.[382] The expansion of quicksilver was long used as the measure of temperature, no clear idea being possessed of temperature apart from some of its more obvious effects. Rumford, in the first experiment leading to a determination of the mechanical equivalent of heat, disregarded the heat absorbed by the apparatus, otherwise he would, in Dr. Joule’s opinion, have come nearly to the correct result.

[382] *Principia*, bk. iii. Prop. 13.

It is surprising to learn the number of causes of error which enter into the simplest experiment, when we strive to attain rigid accuracy. We cannot accurately perform the simple experiment of compressing gas in a bent tube by a column of mercury, in order to test the truth of Boyle’s Law, without paying regard to--(1) the variations of atmospheric pressure, which are communicated to the gas through the mercury; (2) the compressibility of mercury, which causes the column of mercury to vary in density; (3) the temperature of the mercury throughout the column; (4) the temperature of the gas, which is with difficulty maintained invariable; (5) the expansion of the glass tube containing the gas. Although Regnault took all these circumstances into account in his examination of the law,[383] there is no reason to suppose that he exhausted the sources of inaccuracy.

[383] Jamin, *Cours de Physique*, vol. i. pp. 282, 283.

The early investigations concerning the nature of waves in elastic media proceeded upon the assumption that waves of different lengths would travel with equal speed. Newton’s theory of sound led him to this conclusion, and observation (p. 295) had verified the inference. When the undulatory theory came to be applied at the commencement of this century to explain the phenomena of light, a great difficulty was encountered. The angle at which a ray of light is refracted in entering a denser medium depends, according to that theory, on the velocity with which the wave travels, so that if all waves of light were to travel with equal velocity in the same medium, the dispersion of mixed light by the prism and the production of the spectrum could not take place. Some most striking phenomena were thus in direct conflict with the theory. Cauchy first pointed out the explanation, namely, that all previous investigators had made an arbitrary assumption for the sake of simplifying the calculations. They had assumed that the particles of the vibrating medium are so close together that the intervals are inconsiderable compared with the length of the wave. This hypothesis happened to be approximately true in the case of air, so that no error was discovered in experiments on sound. Had it not been so, the earlier analysts would probably have failed to give any solution, and the progress of the subject might have been retarded. Cauchy was able to make a new approximation under the more difficult supposition, that the particles of the vibrating medium are situated at considerable distances, and act and react upon the neighbouring particles by attractive and repulsive forces. To calculate the rate of propagation of disturbance in such a medium is a work of excessive difficulty. The complete solution of the problem appears indeed to be beyond human power, so that we must be content, as in the case of the planetary motions, to look forward to successive approximations. All that Cauchy could do was to show that certain quantities, neglected in previous theories, became of considerable amount under the new conditions of the problem, so that there will exist a relation between the length of the wave, and the velocity at which it travels. To remove, then, the difficulties in the way of the undulatory theory of light, a new approach to probable conditions was needed.[384]

[384] Lloyd’s *Lectures on the Wave Theory*, pp. 22, 23.

In a similar manner Fourier’s theory of the conduction and radiation of heat was based upon the hypothesis that the quantity of heat passing along any line is simply proportional to the rate of change of temperature. But it has since been shown by Forbes that the conductivity of a body diminishes as its temperature increases. All the details of Fourier’s solution therefore require modification, and the results are in the meantime to be regarded as only approximately true.[385]

[385] Tait’s *Thermodynamics*, p. 10.

We ought to distinguish between those problems which are physically and those which are merely mathematically incomplete. In the latter case the physical law is correctly seized, but the mathematician neglects, or is more often unable to follow out the law in all its results. The law of gravitation and the principles of harmonic or undulatory movement, even supposing the data to be correct, can never be followed into all their ultimate results. Young explained the production of Newton’s rings by supposing that the rays reflected from the upper and lower surfaces of a thin film of a certain thickness were in opposite phases, and thus neutralised each other. It was pointed out, however, that as the light reflected from the nearer surface must be undoubtedly a little brighter than that from the further surface, the two rays ought not to neutralise each other so completely as they are observed to do. It was finally shown by Poisson that the discrepancy arose only from incomplete solution of the problem; for the light which has once got into the film must be to a certain extent reflected backwards and forwards *ad infinitum*; and if we follow out this course of the light by perfect mathematical analysis, absolute darkness may be shown to result from the interference of the rays.[386] In this case the natural laws concerned, those of reflection and refraction, are accurately known, and the only difficulty consists in developing their full consequences.

[386] Lloyd’s *Lectures on the Wave Theory*, pp. 82, 83.

*Discovery of Hypothetically Simple Laws.*

In some branches of science we meet with natural laws of a simple character which are in a certain point of view exactly true and yet can never be manifested as exactly true in natural phenomena. Such, for instance, are the laws concerning what is called a *perfect gas*. The gaseous state of matter is that in which the properties of matter are exhibited in the simplest manner. There is much advantage accordingly in approaching the question of molecular mechanics from this side. But when we ask the question--What is a gas? the answer must be a hypothetical one. Finding that gases *nearly* obey the law of Boyle and Mariotte; that they *nearly* expand by heat at the uniform rate of one part in 272·9 of their volume at 0° for each degree centigrade; and that they *more nearly* fulfil these conditions the more distant the point of temperature at which we examine them from the liquefying point, we pass by the principle of continuity to the conception of a perfect gas. Such a gas would probably consist of atoms of matter at so great a distance from each other as to exert no attractive forces upon each other; but for this condition to be fulfilled the distances must be infinite, so that an absolutely perfect gas cannot exist. But the perfect gas is not merely a limit to which we may approach, it is a limit passed by at least one real gas. It has been shown by Despretz, Pouillet, Dulong, Arago, and finally Regnault, that all gases diverge from the Boylean law, and in nearly all cases the density of the gas increases in a somewhat greater ratio than the pressure, indicating a tendency on the part of the molecules to approximate of their own accord. In the more condensable gases such as sulphurous acid, ammonia, and cyanogen, this tendency is strongly apparent near the liquefying point. Hydrogen, on the contrary, diverges from the law of a perfect gas in the opposite direction, that is, the density increases less than in the ratio of the pressure.[387] This is a singular exception, the bearing of which I am unable to comprehend.

[387] Jamin, *Cours de Physique*, vol. i. pp. 283–288.

All gases diverge again from the law of uniform expansion by heat, but the divergence is less as the gas in question is less condensable, or examined at a temperature more removed from its liquefying point. Thus the perfect gas must have an infinitely high temperature. According to Dalton’s law each gas in a mixture retains its own properties unaffected by the presence of any other gas.[388] This law is probably true only by approximation, but it is obvious that it would be true of the perfect gas with infinitely distant particles.[389]

[388] Joule and Thomson, *Philosophical Transactions*, 1854, vol. cxliv. p. 337.

[389] The properties of a perfect gas have been described by Rankine, *Transactions of the Royal Society of Edinburgh*, vol. xxv. p. 561.

*Mathematical Principles of Approximation.*

The approximate character of physical science will be rendered more plain if we consider it from a mathematical point of view. Throughout quantitative investigations we deal with the relation of one quantity to other quantities, of which it is a function; but the subject is sufficiently complicated if we view one quantity as a function of one other. Now, as a general rule, a function can be developed or expressed as the sum of quantities, the values of which depend upon the successive powers of the variable quantity. If *y* be a function of *x* then we may say that

*y* = A + B*x* + C*x*^{2} + D*x*^{3} + E*x*^{4} ....

In this equation, A, B, C, D, &c., are fixed quantities, of different values in different cases. The terms may be infinite in number or after a time may cease to have any value. Any of the coefficients A, B, C, &c., may be zero or negative; but whatever they be they are fixed. The quantity *x* on the other hand may be made what we like, being variable. Suppose, in the first place, that *x* and *y* are both lengths. Let us assume that 1/10,000 part of an inch is the least that we can take note of. Then when *x* is one hundredth of an inch, we have *x*^{2} = 1/10,000, and if C be less than unity, the term C*x*^{2} will be inappreciable, being less than we can measure. Unless any of the quantities D, E, &c., should happen to be very great, it is evident that all the succeeding terms will also be inappreciable, because the powers of *x* become rapidly smaller in geometrical ratio. Thus when *x* is made small enough the quantity *y* seems to obey the equation

*y* = A + B*x*.

If *x* should be still less, if it should become as small, for instance, as 1/1,000,000 of an inch, and B should not be very great, then *y* would appear to be the fixed quantity A, and would not seem to vary with *x* at all. On the other hand, were x to grow greater, say equal to 1/10 inch, and C not be very small, the term C*x*^{2} would become appreciable, and the law would now be more complicated.

We can invert the mode of viewing this question, and suppose that while the quantity *y* undergoes variations depending on many powers of *x*, our power of detecting the changes of value is more or less acute. While our powers of observation remain very rude we may be unable to detect any change in the quantity at all, that is to say, B*x* may always be too small to come within our notice, just as in former days the fixed stars were so called because they remained at apparently fixed distances from each other. With the use of telescopes and micrometers we become able to detect the existence of some motion, so that the distance of one star from another may be expressed by A + B*x*, the term including *x*^{2} being still inappreciable. Under these circumstances the star will seem to move uniformly, or in simple proportion to the time *x*. With much improved means of measurement it will probably be found that this uniformity of motion is only apparent, and that there exists some acceleration or retardation. More careful investigation will show the law to be more and more complicated than was previously supposed.

There is yet another way of explaining the apparent results of a complicated law. If we take any curve and regard a portion of it free from any kind of discontinuity, we may represent the character of such portion by an equation of the form

*y* = A + B*x* + C*x*^{2} + D*x*^{3} + ....

Restrict the attention to a very small portion of the curve, and the eye will be unable to distinguish its difference from a straight line, which amounts to saying that in the portion examined the term C*x*^{2} has no value appreciable by the eye. Take a larger portion of the curve and it will be apparent that it possesses curvature, but it will be possible to draw a parabola or ellipse so that the curve shall apparently coincide with a portion of that parabola or ellipse. In the same way if we take larger and larger arcs of the curve it will assume the character successively of a curve of the third, fourth, and perhaps higher degrees; that is to say, it corresponds to equations involving the third, fourth, and higher powers of the variable quantity.

We have arrived then at the conclusion that every phenomenon, when its amount can only be rudely measured, will either be of fixed amount, or will seem to vary uniformly like the distance between two inclined straight lines. More exact measurement may show the error of this first assumption, and the variation will then appear to be like that of the distance between a straight line and a parabola or ellipse. We may afterwards find that a curve of the third or higher degrees is really required to represent the variation. I propose to call the variation of a quantity *linear*, *elliptic*, *cubic*, *quartic*, *quintic*, &c., according as it is discovered to involve the first, second, third, fourth, fifth, or higher powers of the variable. It is a general rule in quantitative investigation that we commence by discovering linear, and afterwards proceed to elliptic or more complicated laws of variation. The approximate curves which we employ are all, according to De Morgan’s use of the name, parabolas of some order or other; and since the common parabola of the second order is approximately the same as a very elongated ellipse, and is in fact an infinitely elongated ellipse, it is convenient and proper to call variation of the second order *elliptic*. It might also be called *quadric* variation.

As regards many important phenomena we are yet only in the first stage of approximation. We know that the sun and many so-called fixed stars, especially 61 Cygni, have a proper motion through space, and the direction of this motion at the present time is known with some degree of accuracy. But it is hardly consistent with the theory of gravity that the path of any body should really be a straight line. Hence, we must regard a rectilinear path as only a provisional description of the motion, and look forward to the time when its curvature will be detected, though centuries perhaps must first elapse.

We are accustomed to assume that on the surface of the earth the force of gravity is uniform, because the variation is of so slight an amount that we are scarcely able to detect it. But supposing we could measure the variation, we should find it simply proportional to the height. Taking the earth’s radius to be unity, let *h* be the height at which we measure the force of gravity. Then by the well-known law of the inverse square, that force will be proportional to

*g*/(1 + *h*)^{2}, or to *g*(1 - 2*h* + 3*h*^{2} - 4*h*^{3} + ...).

But at all heights to which we can attain *h* will be so small a fraction of the earth’s radius that 3*h*^{2} will be inappreciable, and the force of gravity will seem to follow the law of linear variation, being proportional to 1 - 2*h*.

When the circumstances of an experiment are much altered, different powers of the variable may become prominent. The resistance of a liquid to a body moving through it may be approximately expressed as the sum of two terms respectively involving the first and second powers of the velocity. At very low velocities the first power is of most importance, and the resistance, as Professor Stokes has shown, is nearly in simple proportion to the velocity. When the motion is rapid the resistance increases in a still greater degree, and is more nearly proportional to the square of the velocity.

*Approximate Independence of Small Effects.*

One result of the theory of approximation possesses such importance in physical science, and is so often applied, that we may consider it separately. The investigation of causes and effects is immensely simplified when we may consider each cause as producing its own effect invariably, whether other causes are acting or not. Thus, if the body P produces *x*, and Q produces *y*, the question is whether P and Q acting together will produce the sum of the separate effects, *x* + *y*. It is under this supposition that we treated the methods of eliminating error (Chap. XV.), and errors of a less amount would still remain if the supposition was a forced one. There are probably some parts of science in which the supposition of independence of effects holds rigidly true. The mutual gravity of two bodies is entirely unaffected by the presence of other gravitating bodies. People do not usually consider that this important principle is involved in such a simple thing as putting two pound weights in the scale of a balance. How do we know that two pounds together will weigh twice as much as one? Do we know it to be exactly so? Like other results founded on induction we cannot prove it absolutely, but all the calculations of physical astronomy proceed upon the assumption, so that we may consider it proved to a very high degree of approximation. Had not this been true, the calculations of physical astronomy would have been infinitely more complex than they actually are, and the progress of knowledge would have been much slower.

It is a general principle of scientific method that if effects be of small amount, comparatively to our means of observation, all joint effects will be of a higher order of smallness, and may therefore be rejected in a first approximation. This principle was employed by Daniel Bernoulli in the theory of sound, under the title of *The Principle of the Coexistence of Small Vibrations*. He showed that if a string is affected by two kinds of vibrations, we may consider each to be going on as if the other did not exist. We cannot perceive that the sounding of one musical instrument prevents or even modifies the sound of another, so that all sounds would seem to travel through the air, and act upon the ear in independence of each other. A similar assumption is made in the theory of tides, which are great waves. One wave is produced by the attraction of the moon, and another by the attraction of the sun, and the question arises, whether when these waves coincide, as at the time of spring tides, the joint wave will be simply the sum of the separate waves. On the principle of Bernoulli this will be so, because the tides on the ocean are very small compared with the depth of the ocean.

The principle of Bernoulli, however, is only approximately true. A wave never is exactly the same when another wave is interfering with it, but the less the displacement of particles due to each wave, the less in a still higher degree is the effect of one wave upon the other. In recent years Helmholtz was led to suspect that some of the phenomena of sound might after all be due to resultant effects overlooked by the assumption of previous physicists. He investigated the secondary waves which would arise from the interference of considerable disturbances, and was able to show that certain summation of resultant tones ought to be heard, and experiments subsequently devised for the purpose showed that they might be heard.

[Illustration]

Throughout the mechanical sciences the *Principle of the Superposition of Small Motions* is of fundamental importance,[390] and it may be thus explained. Suppose that two forces, acting from the points B and C, are simultaneously moving a body A. Let the force acting from B be such that in one second it would move A to *p*, and similarly let the second force, acting alone, move A to *r*. The question arises, then, whether their joint action will urge A to *q* along the diagonal of the parallelogram. May we say that A will move the distance A*p* in the direction AB, and A*r* in the direction AC, or, what is the same thing, along the parallel line *pq*? In strictness we cannot say so; for when A has moved towards *p*, the force from C will no longer act along the line AC, and similarly the motion of A towards *r* will modify the action of the force from B. This interference of one force with the line of action of the other will evidently be greater the larger is the extent of motion considered; on the other hand, as we reduce the parallelogram A*pqr*, compared with the distances AB and AC, the less will be the interference of the forces. Accordingly mathematicians avoid all error by considering the motions as infinitely small, so that the interference becomes of a still higher order of infinite smallness, and may be entirely neglected. By the resources of the differential calculus it is possible to calculate the motion of the particle A, as if it went through an infinite number of infinitely small diagonals of parallelograms. The great discoveries of Newton really arose from applying this method of calculation to the movements of the moon round the earth, which, while constantly tending to move onward in a straight line, is also deflected towards the earth by gravity, and moves through an elliptic curve, composed as it were of the infinitely small diagonals of infinitely numerous parallelograms. The mathematician, in his investigation of a curve, always treats it as made up of a great number of straight lines, and it may be doubted whether he could treat it in any other manner. There is no error in the final results, because having obtained the formulæ flowing from this supposition, each straight line is then regarded as becoming infinitely small, and the polygonal line becomes undistinguishable from a perfect curve.[391]

[390] Thomson and Tait’s *Natural Philosophy*, vol. i. p. 60.

[391] Challis, *Notes on the Principles of Pure and Applied Calculation*, 1869, p. 83.

In abstract mathematical theorems the approximation to absolute truth is perfect, because we can treat of infinitesimals. In physical science, on the contrary, we treat of the least quantities which are perceptible. Nevertheless, while carefully distinguishing between these two different cases, we may fearlessly apply to both the principle of the superposition of small effects. In physical science we have only to take care that the effects really are so small that any joint effect will be unquestionably imperceptible. Suppose, for instance, that there is some cause which alters the dimensions of a body in the ratio of 1 to 1 + α, and another cause which produces an alteration in the ratio of 1 to 1 + β. If they both act at once the change will be in the ratio of 1 to (1 + α)(1 + β), or as 1 to 1 + α + β + αβ. But if α and β be both very small fractions of the total dimensions, αβ will be yet far smaller and may be disregarded; the ratio of change is then approximately that of 1 to 1 + α + β, or the joint effect is the sum of the separate effects. Thus if a body were subjected to three strains, at right angles to each other, the total change in the volume of the body would be approximately equal to the sum of the changes produced by the separate strains, provided that these are very small. In like manner not only is the expansion of every solid and liquid substance by heat approximately proportional to the change of temperature, when this change is very small in amount, but the cubic expansion may also be considered as being three times as great as the linear expansion. For if the increase of temperature expands a bar of metal in the ratio of 1 to 1 + α, and the expansion be equal in all directions, then a cube of the same metal would expand as 1 to (1 + α)^{3}, or as 1 to 1 + 3α + 3α^{2} + α^{3}. When α is a very small quantity the third term 3α^{2} will be imperceptible, and still more so the fourth term α^{3}. The coefficients of expansion of solids are in fact so small, and so imperfectly determined, that physicists seldom take into account their second and higher powers.

It is a result of these principles that all small errors may be assumed to vary in simple proportion to their causes--a new reason why, in eliminating errors, we should first of all make them as small as possible. Let us suppose that there is a right-angled triangle of which the two sides containing the right angle are really of the lengths 3 and 4, so that the hypothenuse is √(3^{2} + 4^{2}) or 5. Now, if in two measurements of the first side we commit slight errors, making it successively 4·001 and 4·002, then calculation will give the lengths of the hypothenuse as almost exactly 5·0008 and 5·0016, so that the error in the hypothenuse will seem to vary in simple proportion to that of the side, although it does not really do so with perfect exactness. The logarithm of a number does not vary in proportion to that number--nevertheless we find the difference between the logarithms of the numbers 100000 and 100001 to be almost exactly equal to that between the numbers 100001 and 100002. It is thus a general rule that very small differences between successive values of a function are approximately proportional to the small differences of the variable quantity.

On these principles it is easy to draw up a series of rules such as those given by Kohlrausch[392] for performing calculations in an abbreviated form when the variable quantity is very small compared with unity. Thus for 1 ÷ (1 + α) we may substitute 1 - α; for 1 ÷ (1 - α) we may put 1 + α; 1 ÷ √(1 + α) becomes 1 - (1/2)α, and so forth.

[392] *An Introduction to Physical Measurements*, translated by Waller and Procter, 1873, p. 10.

*Four Meanings of Equality.*

Although it might seem that there are few terms more free from ambiguity than the term *equal*, yet scientific men do employ it with at least four meanings, which it is desirable to distinguish. These meanings I may describe as

(1) Absolute Equality. (2) Sub-equality. (3) Apparent Equality. (4) Probable Equality.

By *absolute equality* we signify that which is complete and perfect to the last degree; but it is obvious that we can only know such equality in a theoretical or hypothetical manner. The areas of two triangles standing upon the same base and between the same parallels are absolutely equal. Hippocrates beautifully proved that the area of a lunula or figure contained between two segments of circles was absolutely equal to that of a certain right-angled triangle. As a general rule all geometrical and other elementary mathematical theorems involve absolute equality.

De Morgan proposed to describe as *sub-equal* those quantities which are equal within an infinitely small quantity, so that *x* is sub-equal to *x* + *dx*. The differential calculus may be said to arise out of the neglect of infinitely small quantities, and in mathematical science other subtle distinctions may have to be drawn between kinds of equality, as De Morgan has shown in a remarkable memoir “On Infinity; and on the sign of Equality.”[393]

[393] *Cambridge Philosophical Transactions* (1865), vol. xi. Part I.

*Apparent equality* is that with which physical science deals. Those magnitudes are apparently equal which differ only by an imperceptible quantity. To the carpenter anything less than the hundredth part of an inch is non-existent; there are few arts or artists to which the hundred-thousandth of an inch is of any account. Since all coincidence between physical magnitudes is judged by one or other sense, we must be restricted to a knowledge of apparent equality.

In reality even apparent equality is rarely to be expected. More commonly experiments will give only *probable equality*, that is results will come so near to each other that the difference may be ascribed to unimportant disturbing causes. Physicists often assume quantities to be equal provided that they fall within the limits of probable error of the processes employed. We cannot expect observations to agree with theory more closely than they agree with each other, as Newton remarked of his investigations concerning Halley’s Comet.

*Arithmetic of Approximate Quantities.*

Considering that almost all the quantities which we treat in physical and social science are approximate only, it seems desirable that attention should be paid in the teaching of arithmetic to the correct interpretation and treatment of approximate numerical statements. We seem to need notation for expressing the approximateness or exactness of decimal numbers. The fraction ·025 may mean either precisely one 40th part, or it may mean anything between ·0245 and ·0255. I propose that when a decimal fraction is completely and exactly given, a *small cipher* or circle should be added to indicate that there is nothing more to come, as in ·025◦. When the first figure of the decimals rejected is 5 or more, the first figure retained should be raised by a unit, according to a rule approved by De Morgan, and now generally recognised. To indicate that the fraction thus retained is more than the truth, a point has been placed over the last figure in some tables of logarithms; but a similar point is used to denote the period of a repeating decimal, and I should therefore propose to employ a colon *after* the figure; thus ·025: would mean that the true quantity lies between ·0245° and ·025° inclusive of the lower but not the higher limit. When the fraction is less than the truth, two dots might be placed horizontally as in 025.. which would mean anything between ·025° and ·0255° not inclusive.

When approximate numbers are added, subtracted, multiplied, or divided, it becomes a matter of some complexity to determine the degree of accuracy of the result. There are few persons who could assert off-hand that the sum of the approximate numbers 34·70, 52·693, 80·1, is 167·5 *within less than* ·07. Mr. Sandeman has traced out the rules of approximate arithmetic in a very thorough manner, and his directions are worthy of careful attention.[394] The third part of Sonnenschein and Nesbitt’s excellent book on arithmetic[395] describes fully all kinds of approximate calculations, and shows both how to avoid needless labour and how to take proper account of inaccuracy in operating with approximate decimal fractions. A simple investigation of the subject is to be found in Sonnet’s *Algèbre Elémentaire* (Paris, 1848) chap. xiv., “Des Approximations Absolues et Relatives.” There is also an American work on the subject.[396]

[394] Sandeman, *Pelicotetics*, p. 214.

[395] *The Science and Art of Arithmetic for the Use of Schools.* (Whitaker and Co.)

[396] *Principles of Approximate Calculations*, by J. J. Skinner, C.E. (New York, Henry Holt), 1876.

Although the accuracy of measurement has so much advanced since the time of Leslie, it is not superfluous to repeat his protest against the unfairness of affecting by a display of decimal fractions a greater degree of accuracy than the nature of the case requires and admits.[397] I have known a scientific man to register the barometer to a second of time when the nearest quarter of an hour would have been amply sufficient. Chemists often publish results of analysis to the ten-thousandth or even the millionth part of the whole, when in all probability the processes employed cannot be depended on beyond the hundredth part. It is seldom desirable to give more than one place of figures of uncertain amount; but it must be allowed that a nice perception of the degree of accuracy possible and desirable is requisite to save misapprehension and needless computation on the one hand, and to secure all attainable exactness on the other hand.

[397] Leslie, *Inquiry into the Nature of Heat*, p. 505.