CHAPTER XXV.

ACCORDANCE OF QUANTITATIVE THEORIES.

In the preceding chapter we found that facts may be classed under four heads as regards their connection with theory, and our powers of explanation or prediction. The facts hitherto considered were generally of a qualitative rather than a quantitative nature; but when we look exclusively to the quantity of a phenomenon, and the various modes in which we may determine its amount, nearly the same system of classification will hold good. There will, however, be five possible cases:--

(1) We may directly and empirically measure a phenomenon, without being able to explain why it should have any particular quantity, or to connect it by theory with other quantities.

(2) In a considerable number of cases we can theoretically predict the existence of a phenomenon, but are unable to assign its amount, except by direct measurement, or to explain the amount theoretically when thus ascertained.

(3) We may measure a quantity, and afterwards explain it as related to other quantities, or as governed by known quantitative laws.

(4) We may predict the quantity of an effect on theoretical grounds, and afterwards confirm the prediction by direct measurement.

(5) We may indirectly determine the quantity of an effect without being able to verity it by experiment.

These classes of quantitative facts might be illustrated by an immense number of interesting points in the history of physical science. Only a few instances of each class can be given here.

*Empirical Measurements.*

Under the first head of purely empirical measurements, which have not been brought under any theoretical system, may be placed the great bulk of quantitative facts recorded by scientific observers. The tables of numerical results which abound in books on chemistry and physics, the huge quartos containing the observations of public observatories, the multitudinous tables of meteorological observations, which are continually being published, the more abstruse results concerning terrestrial magnetism--such results of measurement, for the most part, remain empirical, either because theory is defective, or the labour of calculation and comparison is too formidable. In the Greenwich Observatory, indeed, the salutary practice has been maintained by the present Astronomer Royal, of always reducing the observations, and comparing them with the theories of the several bodies. The divergences from theory thus afford material for the discovery of errors or of new phenomena; in short, the observations have been turned to the use for which they were intended. But it is to be feared that other establishments are too often engaged in merely recording numbers of which no real use is made, because the labour of reduction and comparison with theory is too great for private inquirers to undertake. In meteorology, especially, great waste of labour and money is taking place, only a small fraction of the results recorded being ever used for the advancement of the science. For one meteorologist like Quetelet, Dove, or Baxendell, who devotes himself to the truly useful labour of reducing other people’s observations, there are hundreds who labour under the delusion that they are advancing science by loading our book-shelves with numerical tables. It is to be feared, in like manner, that almost the whole bulk of statistical numbers, whether commercial, vital, or moral, is of little scientific value. Purely empirical measurements may have a direct practical value, as when tables of the specific gravity, or strength of materials, assist the engineer; the specific gravities of mixtures of water with acids, alcohols, salts, &c., are useful in chemical manufactories, custom-house gauging, &c.; observations of rainfall are requisite for questions of water supply; the refractive index of various kinds of glass must be known in making achromatic lenses; but in all such cases the use made of the measurements is not scientific but practical. It may be asserted, that no number which remains isolated, and uncompared by theory with other numbers, is of scientific value. Having tried the tensile strength of a piece of iron in a particular condition, we know what will be the strength of the same kind of iron in a similar condition, provided we can ever meet with that exact kind of iron again; but we cannot argue from piece to piece, nor lay down any laws exactly connecting the strength of iron with the quantity of its impurities.

*Quantities indicated by Theory, but Empirically Measured.*

In many cases we are able to foresee the existence of a quantitative effect, on the ground of general principles, but are unable, either from the want of numerical data, or from the entire absence of any mathematical theory, to assign the amount of such effect. We then have recourse to direct experiment to determine its amount. Whether we argued from the oceanic tides by analogy, or deductively from the theory of gravitation, there could be no doubt that atmospheric tides of some amount must occur in the atmosphere. Theory, however, even in the hands of Laplace, was not able to overcome the complicated mechanical conditions of the atmosphere, and predict the amounts of such tides; and, on the other hand, these amounts were so small, and were so masked by far larger undulations arising from the heating power of the sun, and from other meteorological disturbances, that they would probably have never been discovered by purely empirical observations. Theory having, however, indicated their existence and their periods, it was easy to make series of barometrical observations in places selected so as to be as free as possible from casual fluctuations, and then, by the suitable application of the method of means, to detect the small effects in question. The principal lunar atmospheric tide was thus proved to amount to between ·003 and ·004 inch.[466]

[466] Grant’s *History of Physical Astronomy*, p. 162.

Theory yields the greatest possible assistance in applying the method of means. For if we have a great number of empirical measurements, each representing the joint effect of a number of causes, our object will be to take the mean of all those in which the effect to be measured is present, and compare it with the mean of the remainder in which the effect is absent, or acts in the opposite direction. The difference will then represent the amount of the effect, or double the amount respectively. Thus, in the case of the atmospheric tides, we take the mean of all the observations when the moon was on the meridian, and compare it with the mean of all observations when she was on the horizon. In this case we trust to chance that all other effects will lie about as often in one direction as the other, and will neutralise themselves in the drawing of each mean. It is a great advantage, however, to be able to decide by theory when each principal disturbing effect is present or absent; for the means may then be drawn so as to separate each such effect, leaving only minor and casual divergences to the law of error. Thus, if there be three principal effects, and we draw means giving respectively the sum of all three, the sum of the first two, and the sum of the last two, then we gain three simple equations, by the solution of which each quantity is determined.

*Explained Results of Measurement.*

The second class of measured phenomena contains those which, after being determined in a direct and purely empirical application of measuring instruments, are afterwards shown to agree with some hypothetical explanation. Such results are turned to their proper use, and several advantages may arise from the comparison. The correspondence with theory will seldom or never be precise; and, even if it be so, the coincidence must be regarded as accidental.

If the divergences between theory and experiment be comparatively small, and variable in amount and direction, they may often be safely attributed to inconsiderable sources of error in the experimental processes. The strict method of procedure is to calculate the probable error of the mean of the observed results (p. 387), and then observe whether the theoretical result falls within the limits of probable error. If it does, and if the experimental results agree as well with theory as they agree with each other, then the probability of the theory is much increased, and we may employ the theory with more confidence in the anticipation of further results. The probable error, it should be remembered, gives a measure only of the effects of incidental and variable sources of error, but in no degree indicates the amount of fixed causes of error. Thus, if the mean results of two modes of determining a quantity are so far apart that the limits of probable error do not overlap, we may infer the existence of some overlooked source of fixed error in one or both modes. We will further consider in a subsequent section the discordance of measurements.

*Quantities determined by Theory and verified by Measurement.*

One of the most satisfactory tests of a theory consists in its application not only to predict the nature of a phenomenon, and the circumstances in which it may be observed, but also to assign the precise quantity of the phenomenon. If we can subsequently apply accurate instruments and measure the amount of the phenomenon witnessed, we have an excellent opportunity of verifying or negativing the theory. It was in this manner that Newton first attempted to verify his theory of gravitation. He knew approximately the velocity produced in falling bodies at the earth’s surface, and if the law of the inverse square of the distance held true, and the reputed distance of the moon was correct, he could infer that the moon ought to fall towards the earth at the rate of fifteen feet in one minute. Now, the actual divergence of the moon from the tangent of its orbit appeared to amount only to thirteen feet in one minute, and there was a discrepancy of two feet in fifteen, which caused Newton to lay “aside at that time any further thoughts of this matter.” Many years afterwards, probably fifteen or sixteen years, Newton obtained more precise data from which he could calculate the size of the moon’s orbit, and he then found the discrepancy to be inconsiderable.

His theory of gravitation was thus verified as far as the moon was concerned; but this was to him only the beginning of a long course of deductive calculations, each ending in a verification. If the earth and moon attract each other, and also the sun and the earth, there is reason to expect that the sun and moon should attract each other. Newton followed out the consequences of this inference, and showed that the moon would not move as if attracted by the earth only, but sometimes faster and sometimes slower. Comparison with Flamsteed’s observations of the moon showed that such was the case. Newton argued again, that as the waters of the ocean are not rigidly attached to the earth, they might attract the moon, and be attracted in return, independently of the rest of the earth. Certain daily motions resembling the tides would then be caused, and there were the tides to verify the reasoning. It was the extraordinary power with which Newton traced out geometrically the consequences of his theory, and submitted them to repeated comparison with experience, which constitutes his pre-eminence over all physicists.

*Quantities determined by Theory and not verified.*

It will continually happen that we are able, from certain measured phenomena and a correct theory, to determine the amount of some other phenomenon which we may either be unable to measure at all, or to measure with an accuracy corresponding to that required to verify the prediction. Thus Laplace having worked out a theory of the motions of Jupiter’s satellites on the hypothesis of gravitation, found that these motions were greatly affected by the spheroidal form of Jupiter. The motions of the satellites can be observed with great accuracy owing to their frequent eclipses and transits, and from these motions he was able to argue inversely, and assign the ellipticity of the planet. The ratio of the polar and equatorial axes thus determined was very nearly that of 13 to 14; and it agrees well with such direct micrometrical measurements of the planet as have been made; but Laplace believed that the theory gave a more accurate result than direct observation could yield, so that the theory could hardly be said to admit of direct verification.

The specific heat of air was believed on the grounds of direct experiment to amount to 0·2669, the specific heat of water being taken as unity; but the methods of experiment were open to considerable causes of error. Rankine showed in 1850 that it was possible to calculate from the mechanical equivalent of heat and other thermodynamic data, what this number should be, and he found it to be 0·2378. This determination was at the time accepted as the most satisfactory result, although not verified; subsequently in 1853 Regnault obtained by direct experiment the number 0·2377, proving that the prediction had been well grounded.

It is readily seen that in quantitative questions verification is a matter of degree and probability. A less accurate method of measurement cannot verify the results of a more accurate method, so that if we arrive at a determination of the same physical quantity in several distinct modes it is often a delicate matter to decide which result is most reliable, and should be used for the indirect determination of other quantities. For instance, Joule’s and Thomson’s ingenious experiments upon the thermal phenomena of fluids in motion[467] involved, as one physical constant, the mechanical equivalent of heat; if requisite, then, they might have been used to determine that important constant. But if more direct methods of experiment give the mechanical equivalent of heat with superior accuracy, then the experiments on fluids will be turned to a better use in determining various quantities relating to the theory of fluids. We will further consider questions of this kind in succeeding sections.

[467] *Philosophical Transactions* (1854), vol. cxliv. p. 364.

There are of course many quantities assigned on theoretical grounds which we are quite unable to verify with corresponding accuracy. The thickness of a film of gold leaf, the average depths of the oceans, the velocity of a star’s approach to or regression from the earth as inferred from spectroscopic data (pp. 296–99), are cases in point; but many others might be quoted where direct verification seems impossible. Newton and subsequent physicists have measured light undulations, and by several methods we learn the velocity with which light travels. Since an undulation of the middle green is about five ten-millionths of a metre in length, and travels at the rate of nearly 300,000,000 of metres per second, it follows that about 600,000,000,000,000 undulations must strike in one second the retina of an eye which perceives such light. But how are we to verify such an astounding calculation by directly counting pulses which recur six hundred billions of times in a second?

*Discordance of Theory and Experiment.*

When a distinct want of accordance is found to exist between the results of theory and direct measurement, interesting questions arise as to the mode in which we can account for this discordance. The ultimate explanation of the discrepancy may be accomplished in at least four ways as follows:--

(1) The direct measurement may be erroneous owing to various sources of casual error.

(2) The theory may be correct as far as regards the general form of the supposed laws, but some of the constant numbers or other quantitative data employed in the theoretical calculations may be inaccurate.

(3) The theory may be false, in the sense that the forms of the mathematical equations assumed to express the laws of nature are incorrect.

(4) The theory and the involved quantities may be approximately accurate, but some regular unknown cause may have interfered, so that the divergence may be regarded as a *residual effect* representing possibly a new and interesting phenomenon.

No precise rules can be laid down as to the best mode of proceeding to explain the divergence, and the experimentalist will have to depend upon his own insight and knowledge; but the following recommendations may be made.

If the experimental measurements are not numerous, repeat them and take a more extensive mean result, the probable accuracy of which, as regards casual errors, will increase as the square root of the number of experiments. Supposing that no considerable modification of the result is thus effected, we may suspect the existence of more deep-seated sources of error in our method of measurement. The next resource will be to change the size and form of the apparatus employed, and to introduce various modifications in the materials employed or the course of procedure, in the hope (p. 396) that some cause of constant error may thus be removed. If the inconsistency with theory still remains unreduced we may attempt to invent some widely different mode of arriving at the same physical quantity, so that we may be almost sure that the same cause of error will not affect both the new and old results. In some cases it is possible to find five or six essentially different modes of arriving at the same determination.

Supposing that the discrepancy still exists we may begin to suspect that our direct measurements are correct, and that the data employed in the theoretical calculations are inaccurate. We must now review the grounds on which these data depend, consisting as they must ultimately do of direct measurements. A comparison of the recorded data will show the degree of probability attaching to the mean result employed; and if there is any ground for imagining the existence of error, we should repeat the observations, and vary the forms of experiment just as in the case of the previous direct measurements. The continued existence of the discrepancy must show that we have not attained to a complete acquaintance with the theory of the causes in action, but two different cases still remain. We may have misunderstood the action of those causes which we know to exist, or we may have overlooked the existence of one or more other causes. In the first case our hypothesis appears to be wrongly chosen and inapplicable; but whether we are to reject it will depend upon whether we can form another hypothesis which yields a more accurate accordance. The probability of an hypothesis, it will be remembered (p. 243), is to be judged, in the absence of *à priori* grounds of judgment, by the probability that if the supposed causes exist the observed result follows; but as there is now little probability of reconciling the original hypothesis with our direct measurements the field is open for new hypotheses, and any one which gives a closer accordance with measurement will so far have better claims to attention. Of course we must never estimate the probability of an hypothesis merely by its accordance with a few results only. Its general analogy and accordance with other known laws of nature, and the fact that it does not conflict with other probable theories, must be taken into account, as we shall see in the next book. The requisite condition of a good hypothesis, that it must admit of the deduction of facts verified in observation, must be interpreted in the widest manner, as including all ways in which there may be accordance or discordance. All our attempts at reconciliation having failed, the only conclusion we can come to is that some unknown cause of a new character exists. If the measurements be accurate and the theory probable, then there remains a *residual phenomenon*, which, being devoid of theoretical explanation, must be set down as a new empirical fact worthy of further investigation. Outstanding residual discrepancies have often been found to involve new discoveries of the greatest importance.

*Accordance of Measurements of Astronomical Distances.*

One of the most instructive instances which we can meet, of the manner in which different measurements confirm or check each other, is furnished by the determination of the velocity of light, and the dimensions of the planetary system. Roemer first discovered that light requires time to travel, by observing that the eclipses of Jupiter’s satellites, although they occur at fixed moments of absolute time, are visible at different moments in different parts of the earth’s orbit, according to the distance between the earth and Jupiter. The time occupied by light in traversing the mean semi-diameter of the earth’s orbit is found to be about eight minutes. The mean distance of the sun and earth was long assumed by astronomers as being about 95,274,000 miles, this result being deduced by Bessel from the observations of the transit of Venus, which occurred in 1769, and which were found to give the solar parallax, or which is the same thing, the apparent angular magnitude of the earth seen from the sun, as equal to 8″·578. Dividing the mean distance of the sun and earth by the number of seconds in 8^{m}. 13^{s}.3 we find the velocity of light to be about 192,000 miles per second.

Nearly the same result was obtained in what seems a different manner. The aberration of light is the apparent change in the direction of a ray of light owing to the composition of its motion with that of the earth’s motion round the sun. If we know the amount of aberration and the mean velocity of the earth, we can estimate that of light, which is thus found to be 191,100 miles per second. Now this determination depends upon a new physical quantity, that of aberration, which is ascertained by direct observation of the stars, so that the close accordance of the estimates of the velocity of light as thus arrived at by different methods might seem to leave little room for doubt, the difference being less than one per cent.

Nevertheless, experimentalists were not satisfied until they had succeeded in measuring the velocity of light by direct experiments performed upon the earth’s surface. Fizeau, by a rapidly revolving toothed wheel, estimated the velocity at 195,920 miles per second. As this result differed by about one part in sixty from estimates previously accepted, there was thought to be room for further investigation. The revolving mirror, used by Wheatstone in measuring the velocity of electricity, was now applied in a more refined manner by Fizeau and by Foucault to determine the velocity of light. The latter physicist came to the startling conclusion that the velocity was not really more than 185,172 miles per second. No repetition of the experiment would shake this result, and there was accordingly a discrepancy between the astronomical and the experimental results of about 7,000 miles per second. The latest experiments, those of M. Cornu, only slightly raise the estimate, giving 186,660 miles per second. A little consideration shows that both the astronomical determinations involve the magnitude of the earth’s orbit as one datum, because our estimate of the earth’s velocity in its orbit depends upon our estimate of the sun’s mean distance. Accordingly as regards this quantity the two astronomical results count only for one. Though the transit of Venus had been considered to give the best data for the calculation of the sun’s parallax, yet astronomers had not neglected less favourable opportunities. Hansen, calculating from certain inequalities in the moon’s motion, had estimated it at 8″·916; Winneke, from observations of Mars, at 8″·964; Leverrier, from the motions of Mars, Venus, and the moon, at 8″·950. These independent results agree much better with each other than with that of Bessel (8″·578) previously received, or that of Encke (8″·58) deduced from the transits of Venus in 1761 and 1769, and though each separately might be worthy of less credit, yet their close accordance renders their mean result (8″·943) comparable in probability with that of Bessel. It was further found that if Foucault’s value for the velocity of light were assumed to be correct, and the sun’s distance were inversely calculated from that, the sun’s parallax would be 8″·960, which closely agreed with the above mean result. This further correspondence of independent results threw the balance of probability strongly against the results of the transit of Venus, and rendered it desirable to reconsider the observations made on that occasion. Mr. E. J. Stone, having re-discussed those observations,[468] found that grave oversights had been made in the calculations, which being corrected would alter the estimate of parallax to 8″·91, a quantity in such comparatively close accordance with the other results that astronomers did not hesitate at once to reduce their estimate of the sun’s mean distance from 95,274,000 to 91,771,000, miles, although this alteration involved a corresponding correction in the assumed magnitudes and distances of most of the heavenly bodies. The solar parallax is now (1875) believed to be about 8″·878, the number deduced from Cornu’s experiments on the velocity of light. This result agrees very closely with 8″·879, the estimate obtained from new observations on the transit of Venus, by the French observers, and with 8″·873, the result of Galle’s observations of the planet Flora. When all the observations of the late transit of Venus are fully discussed the sun’s distance will probably be known to less than one part in a thousand, if not one part in ten thousand.[469]

[468] *Monthly Notices of the Royal Astronomical Society*, vol. xxviii. p. 264.

[469] It would seem to be absurd to repeat the profuse expenditure of 1874 at the approaching transit in 1882. The aggregate sum spent in 1874 by various governments and individuals can hardly be less than £200,000, a sum which, wisely expended on scientific investigations, would give a hundred important results.

In this question the theoretical relations between the velocity of light, the constant of aberration, the sun’s parallax, and the sun’s mean distance, are of the simplest character, and can hardly be open to any doubt, so that the only doubt was as to which result of observation was the most reliable. Eventually the chief discrepancy was found to arise from misapprehension in the reduction of observations, but we have a satisfactory example of the value of different methods of estimation in leading to the detection of a serious error. Is it not surprising that Foucault by measuring the velocity of light when passing through the space of a few yards, should lead the way to a change in our estimates of the magnitudes of the whole universe?

*Selection of the best Mode of Measurement.*

When we once obtain command over a question of physical science by comprehending the theory of the subject, we often have a wide choice opened to us as regards the methods of measurement, which may thenceforth be made to give the most accurate results. If we can measure one fundamental quantity very precisely we may be able by theory to determine accurately many other quantitative results. Thus, if we determine satisfactorily the atomic weights of certain elements, we do not need to determine with equal accuracy the composition and atomic weights of their several compounds. Having learnt the relative atomic weights of oxygen and sulphur, we can calculate the composition by weight of the several oxides of sulphur. Chemists accordingly select with the greatest care that compound of two elements which seems to allow of the most accurate analysis, so as to give the ratio of their atomic weights. It is obvious that we only need the ratio of the atomic weight of each element to that of some common element, in order to calculate, that of each to each. Moreover the atomic weight stands in simple relation to other quantitative facts. The weights of equal volumes of elementary gases at equal temperature and pressure have the same ratios as the atomic weights; now, as nitrogen under such circumstances weighs 14·06 times as much as hydrogen, we may infer that the atomic weight of nitrogen is about 14·06, or more probably 14·00, that of hydrogen being unity. There is much evidence, again, that the specific heats of elements are inversely as their atomic weights, so that these two classes of quantitative data throw light mutually upon each other. In fact the atomic weight, the atomic volume, and the atomic heat of an element, are quantities so closely connected that the determination of one will lead to that of the others. The chemist has to solve a complicated problem in deciding in the case of each of 60 or 70 elements which mode of determination is most accurate. Modern chemistry presents us with an almost infinitely extensive web of numerical ratios developed out of a few fundamental ratios.

In hygrometry we have a choice among at least four modes of measuring the quantity of aqueous vapour contained in a given bulk of air. We can extract the vapour by absorption in sulphuric acid, and directly weigh its amount; we can place the air in a barometer tube and observe how much the absorption of the vapour alters the elastic force of the air; we can observe the dew-point of the air, that is the temperature at which the vapour becomes saturated; or, lastly, we can insert a dry and wet bulb thermometer and observe the temperature of an evaporating surface. The results of each mode can be connected by theory with those of the other modes, and we can select for each experiment that mode which is most accurate or most convenient. The chemical method of direct measurement is capable of the greatest accuracy, but is troublesome; the dry and wet bulb thermometer is sufficiently exact for meteorological purposes and is most easy to use.

*Agreement of Distinct Modes of Measurement.*

Many illustrations might be given of the accordance which has been found to exist in some cases between the results of entirely different methods of arriving at the measurement of a physical quantity. While such accordance must, in the absence of information to the contrary, be regarded as the best possible proof of the approximate correctness of the mean result, yet instances have occurred to show that we can never take too much trouble in confirming results of great importance. When three or even more distinct methods have given nearly coincident numbers, a new method has sometimes disclosed a discrepancy which it is yet impossible to explain.

The ellipticity of the earth is known with considerable approach to certainty and accuracy, for it has been estimated in three independent ways. The most direct mode is to measure long arcs extending north and south upon the earth’s surface, by means of trigonometrical surveys, and then to compare the lengths of these arcs with their curvature as determined by observations of the altitude of certain stars at the terminal points. The most probable ellipticity of the earth deduced from all measurements of this kind was estimated by Bessel at 1/300, though subsequent measurements might lead to a slightly different estimate. The divergence from a globular form causes a small variation in the force of gravity at different parts of the earth’s surface, so that exact pendulum observations give the data for an independent estimate of the ellipticity, which is thus found to be 1/320. In the third place the spheroidal protuberance about the earth’s equator leads to a certain inequality in the moon’s motion, as shown by Laplace; and from the amount of that inequality, as given by observations, Laplace was enabled to calculate back to the amount of its cause. He thus inferred that the ellipticity is 1/305, which lies between the two numbers previously given, and was considered by him the most satisfactory determination. In this case the accordance is undisturbed by subsequent results, so that we are obliged to accept Laplace’s result as a highly probable one.

The mean density of the earth is a constant of high importance, because it is necessary for the determination of the masses of all the other heavenly bodies. Astronomers and physicists accordingly have bestowed a great deal of labour upon the exact estimation of this constant. The method of procedure consists in comparing the gravitation of the globe with that of some body of matter of which the mass is known in terms of the assumed unit of mass. This body of matter, serving as an intermediate term of comparison, may be variously chosen; it may consist of a mountain, or a portion of the earth’s crust, or a heavy ball of metal. The method of experiment varies so much according as we select one body or the other, that we may be said to have three independent modes of arriving at the desired result.

The mutual gravitation of two balls is so exceedingly small compared with their gravitation towards the immense mass of the earth, that it is usually quite imperceptible, and although asserted by Newton to exist, on the ground of theory, was never observed until the end of the 18th century. Michell attached two small balls to the extremities of a delicately suspended torsion balance, and then bringing heavy balls of lead alternately to either side of these small balls was able to detect a slight deflection of the torsion balance. He thus furnished a new verification of the theory of gravitation. Cavendish carried out the experiment with more care, and estimated the gravitation of the balls by treating the torsion balance as a pendulum; then taking into account the respective distances of the balls from each other and from the centre of the earth, he was able to assign 5·48 (or as re-computed by Baily, 5·448) as the probable mean density of the earth. Newton’s sagacious guess to the effect that the density of the earth was between five and six times that of water, was thus remarkably confirmed. The same kind of experiment repeated by Reich gave 5·438. Baily having again performed the experiment with every possible refinement obtained a slightly higher number, 5·660.

A different method of procedure consisted in ascertaining the effect of a mountain mass in deflecting the plumb-line; for, assuming that we can determine the dimensions and mean density of the mountain, the plumb-line enables us to compare its mass with that of the whole earth. The mountain Schehallien was selected for the experiment, and observations and calculations performed by Maskelyne, Hutton, and Playfair, gave as the most probable result 4·713. The difference from the experimental results already mentioned is considerable and is important, because the instrumental operations are of an entirely different character from those of Cavendish and Baily’s experiments. Sir Henry James’ similar determination from the attraction of Arthur’s Seat gave 5·14.

A third distinct method consists in determining the force of gravity at points elevated above the surface of the earth on mountain ranges, or sunk below it in mines. Carlini experimented with a pendulum at the hospice of Mont Cenis, 6,375 feet above the sea, and by comparing the attractive forces of the earth and the Alps, found the density to be still smaller, namely, 4·39, or as corrected by Giulio, 4·950. Lastly, the Astronomer Royal has on two occasions adopted the opposite method of observing a pendulum at the bottom of a deep mine, so as to compare the density of the strata penetrated with the density of the whole earth. On the second occasion he carried his method into effect at the Harton Colliery, 1,260 feet deep; all that could be done by skill in measurement and careful consideration of all the causes of error, was accomplished in this elaborate series of observations[470] (p. 291). No doubt Sir George Airy was much perplexed when he found that his new result considerably exceeded that obtained by any other method, being no less than 6·566, or 6·623 as finally corrected. In this case we learn an impressive lesson concerning the value of repeated determinations by distinct methods in disabusing our minds of the reliance which we are only too apt to place in results which show a certain degree of coincidence.

[470] *Philosophical Transactions* (1856), vol. cxlvi. p. 342.

In 1844 Herschel remarked in his memoir of Francis Baily,[471] “that the mean specific gravity of this our planet is, in all human probability, quite as well determined as that of an ordinary hand-specimen in a mineralogical cabinet,--a marvellous result, which should teach us to despair of nothing which lies within the compass of number, weight and measure.” But at the same time he pointed out that Baily’s final result, of which the probable error was only 0·0032, was the highest of all determinations then known, and Airy’s investigation has since given a much higher result, quite beyond the limits of probable error of any of the previous experiments. If we treat all determinations yet made as of equal weight, the simple mean is about 5·45, the mean error nearly 0·5, and the probable error almost 0·2, so that it is as likely as not that the truth lies between 5·65 and 5·25 on this view of the matter. But it is remarkable that the two most recent and careful series of observations by Baily and Airy,[472] lie beyond these limits, and as with the increase of care the estimate rises, it seems requisite to reject the earlier results, and look upon the question as still requiring further investigation. Physicists often take 5-2/3 or 5·67 as the best guess at the truth, but it is evident that new experiments are much required. I cannot help thinking that a portion of the great sums of money which many governments and private individuals spent upon the transit of Venus expeditions in 1874, and which they will probably spend again in 1882 (p. 562), would be better appropriated to new determinations of the earth’s density. It seems desirable to repeat Baily’s experiment in a vacuous case, and with the greater mechanical refinements which the progress of the last forty years places at the disposal of the experimentalist. It would be desirable, also, to renew the pendulum experiments of Airy in some other deep mine. It might even be well to repeat upon some suitable mountain the observations performed at Schehallien. All these operations might be carried out for the cost of one of the superfluous transit expeditions.

[471] *Monthly Notices of the Royal Astronomical Society*, for 8th Nov. 1844, No. X. vol. vi. p. 89.

[472] *Philosophical Magazine*, 2nd Series, vol. xxvi. p. 61.

Since the establishment of the dynamical theory of heat it has become a matter of the greatest importance to determine with accuracy the mechanical equivalent of heat, or the quantity of energy which must be given, or received, in a definite change of temperature effected in a definite quantity of a standard substance, such as water. No less than seven almost entirely distinct modes of determining this constant have been tried. Dr. Joule first ascertained by the friction of water that to raise the temperature of one kilogram of water through one degree centigrade, we must employ energy sufficient to raise 424 kilograms through the height of one metre against the force of gravity at the earth’s surface. Joule, Mayer, Clausius,[473] Favre and other experimentalists have made determinations by less direct methods. Experiments on the mechanical properties of gases give 426 kilogrammetres as the constant; the work done by a steam-engine gives 413; from the heat evolved in electrical experiments several determinations have been obtained; thus from induced electric currents we get 452; from the electro-magnetic engine 443; from the circuit of a battery 420; and, from an electric current, the lowest result of all, namely, 400.[474]

[473] Clausius in *Philosophical Magazine*, 4th Series, vol. ii. p. 119.

[474] Watts’ *Dictionary of Chemistry*, vol. iii. p. 129.

Considering the diverse and in many cases difficult methods of observation, these results exhibit satisfactory accordance, and their mean (423·9) comes very close to the number derived by Dr. Joule from the apparently most accurate method. The constant generally assumed as the most probable result is 423·55 kilogrammetres.

*Residual Phenomena.*

Even when the experimental data employed in the verification of a theory are sufficiently accurate, and the theory itself is sound, there may exist discrepancies demanding further investigation. Herschel pointed out the importance of such outstanding quantities, and called them *residual phenomena*.[475] Now if the observations and the theory be really correct, such discrepancies must be due to the incompleteness of our knowledge of the causes in action, and the ultimate explanation must consist in showing that there is in action, either

[475] *Preliminary Discourse*, §§ 158, 174. *Outlines of Astronomy*, 4th edit. § 856.

(1) Some agent of known nature whose presence was not suspected;

Or (2) Some new agent of unknown nature.

In the first case we can hardly be said to make a new discovery, for our ultimate success consists merely in reconciling the theory with known facts when our investigation is more comprehensive. But in the second case we meet with a totally new fact, which may lead us to realms of new discovery. Take the instance adduced by Herschel. The theory of Newton and Halley concerning comets was that they were gravitating bodies revolving round the sun in elliptic orbits, and the return of Halley’s Comet, in 1758, verified this theory. But, when accurate observations of Encke’s Comet came to be made, the verification was not found to be exact. Encke’s Comet returned each time a little sooner than it ought to do, the period regularly decreasing from 1212·79 days, between 1786 and 1789, to 1210·44 between 1855 and 1858; and the hypothesis has been started that there is a resisting medium filling the space through which the comet passes. This hypothesis is a *deus ex machinâ* for explaining this solitary phenomenon, and cannot possess much probability unless it can be shown that other phenomena are deducible from it. Many persons have identified this medium with that through which light undulations pass, but I am not aware that there is anything in the undulatory theory of light to show that the medium would offer resistance to a moving body. If Professor Balfour Stewart can prove that a rotating disc would experience resistance in a vacuous receiver, here is an experimental fact which distinctly supports the hypothesis. But in the mean time it is open to question whether other known agents, for instance electricity, may not be brought in, and I have tried to show that if, as is believed, the tail of a comet is an electrical phenomenon, it is a necessary result of the conservation of energy that the comet shall exhibit a loss of energy manifested in a diminution of its mean distance from the sun and its period of revolution.[476] It should be added that if Professor Tait’s theory be correct, as seems very probable, and comets consist of swarms of small meteors, there is no difficulty in accounting for the retardation. It has long been known that a collection of small bodies travelling together in an orbit round a central body will tend to fall towards it. In either case, then, this residual phenomenon seems likely to be reconciled with known laws of nature.

[476] *Proceedings of the Manchester Literary and Philosophical Society*, 28th November, 1871, vol. xi. p. 33. Since the above remarks were written, Professor Balfour Stewart has pointed out to me his paper in the *Proceedings of the Manchester Literary and Philosophical Society* for 15th November, 1870 (vol. x. p. 32), in which he shows that a body moving in an enclosure of uniform temperature would probably experience resistance independently of the presence of a ponderable medium, such as gas, between the moving body and the enclosure. The proof is founded on the theory of the dissipation of energy, and this view is said to be accepted by Professors Thomson and Tait. The enclosure is used in this case by Professor Stewart simply as a means of obtaining a proof, just as it was used by him on a previous occasion to obtain a proof of certain consequences of the Theory of Exchanges. He is of opinion that in both of these cases when once the proof has been obtained, the enclosure may be dispensed with. We know, for instance, that the relation between the inductive and absorptive powers of bodies--although this relation may have been proved by means of an enclosure, does not depend upon its presence, and Professor Stewart thinks that in like manner two bodies, or at least two bodies possessing heat such as the sun and the earth in motion relative to each other, will have the differential motion retarded until perhaps it is ultimately destroyed.

In other cases residual phenomena have involved important inferences not recognised at the time. Newton showed how the velocity of sound in the atmosphere could be calculated by a theory of pulses or undulations from the observed tension and density of the air. He inferred that the velocity in the ordinary state of the atmosphere at the earth’s surface would be 968 feet per second, and rude experiments made by him in the cloisters of Trinity College seemed to show that this was not far from the truth. Subsequently it was ascertained by other experimentalists that the velocity of sound was more nearly 1,142 feet, and the discrepancy being one-sixth part of the whole was far too much to attribute to casual errors in the numerical data. Newton attempted to explain away this discrepancy by hypotheses as to the reactions of the molecules of air, but without success.

New investigations having been made from time to time concerning the velocity of sound, both as observed experimentally and as calculated from theory, it was found that each of Newton’s results was inaccurate, the theoretical velocity being 916 feet per second, and the real velocity about 1,090 feet. The discrepancy, nevertheless, remained as serious as ever, and it was not until the year 1816 that Laplace showed it to be due to the heat developed by the sudden compression of the air in the passage of the wave, this heat having the effect of increasing the elasticity of the air and accelerating the impulse. It is now perceived that this discrepancy really involves the doctrine of the equivalence of heat and energy, and it was applied by Mayer, at least by implication, to give an estimate of the mechanical equivalent of heat. The estimate thus derived agrees satisfactorily with direct determinations by Dr. Joule and other physicists, so that the explanation of the residual phenomenon which exercised Newton’s ingenuity is now complete, and forms an important part of the new science of thermodynamics.

As Herschel observed, almost all great astronomical discoveries have been disclosed in the form of residual differences. It is the practice at well-conducted observatories to compare the positions of the heavenly bodies as actually observed with what might have been expected theoretically. This practice was introduced by Halley when Astronomer Royal, and his reduction of the lunar observations gave a series of residual errors from 1722 to 1739, by the examination of which the lunar theory was improved. Most of the greater astronomical variations arising from nutation, aberration, planetary perturbation were discovered in the same manner. The precession of the equinox was perhaps the earliest residual difference observed; the systematic divergence of Uranus from its calculated places was one of the latest, and was the clue to the remarkable discovery of Neptune. We may also class under residual phenomena all the so-called *proper motions* of the stars. A complete star catalogue, such as that of the British Association, gives a greater or less amount of proper motion for almost every star, consisting in the apparent difference of position of the star as derived from the earliest and latest good observations. But these apparent motions are often due, as explained by Baily,[477] the author of the catalogue, to errors of observation and reduction. In many cases the best astronomical authorities have differed as to the very direction of the supposed proper motion of stars, and as regards the amount of the motion, for instance of α Polaris, the most different estimates have been formed. Residual quantities will often be so small that their very existence is doubtful. Only the gradual progress of theory and of measurement will show clearly whether a discrepancy is to be referred to casual errors of observation or to some new phenomenon. But nothing is more requisite for the progress of science than the careful recording and investigation of such discrepancies. In no part of physical science can we be free from exceptions and outstanding facts, of which our present knowledge can give no account. It is among such anomalies that we must look for the clues to new realms of facts worthy of discovery. They are like the floating waifs which led Columbus to suspect the existence of the new world.

[477] *British Association Catalogue of Stars*, p. 49.