Popular Science Monthly/Volume 12/January 1878/History of the Dynamical Theory of Heat II
By PORTER POINIER.
ABOUT one year after the reading of the famous paper of Rumford, in the early part of 1799, Sir Humphry Davy, then but twenty years of age, published his first scientific memoir, entitled "An Essay on Heat, Light, and the Combinations of Light." Clearly enunciating the two systems of hypothesis previously held, he chose to follow Newton in rejecting the materiality of heat, while still clinging to the corpuscular or emission theory of light.
His position with respect to the existence of caloric he asserted in this thesis:
"The Phenomena of Repulsion are not dependent on a peculiar Elastic Fluid for their Existence, or Caloric does not exist;" proceeding to maintain it by a series of experimental reductio ad absurdum.
Premising that the temperature of a body could not be increased unless either its "capacity" were diminished from some cause, or heat were added to it from still other bodies in contact, and observing a production of heat to be consequent on friction or percussion, he enumerated the following as including all possible explanations of the phenomenon consistent with the assumption of caloric:
First, the production by the friction of a specific diminution in the "capacity" of the body, whereby caloric would be disengaged, and thus made sensible. This was the supposition which Count Rumford showed to be quite incompatible with the inexhaustibility of the supply.
Second, the liberation of caloric during some slow process of combustion accompanying the friction, the source in this case being the oxygen of the surrounding medium. This contingency was likewise anticipated by Rumford, who failed to detect any indications of such an action.
And, third, the production of some occult change in the bodies rubbed, whereby they might acquire the property of abstracting an unusual quantity of heat-substance from surrounding matter.
His argument against the existence of caloric depended, therefore, upon showing that these different suppositions were all contrary to the indications of experiment, whence the inference as to the untenability of the hypothesis itself. But, although this method of reasoning has been characterized as "somewhat confused," the following experiments upon which it was based are now considered classical.
Two parallelopipedons of ice, initially at a temperature of 29° Fahr., were fastened in an apparatus by which they might be rubbed together, and kept in a continued and violent friction with each other. They thus were almost wholly melted, the temperature of the resulting water being "ascertained to be 35°, after remaining in an atmosphere of a lower temperature for some minutes." The fusion also was observed to take place only at the rubbing surface.
From this experiment it was therefore to be inferred that the "capacity" of a body was not necessarily diminished by friction; for, according to the discoveries of Black, the melting of a quantity of ice could only take place with the absorption of a definite quantity of heat—its latent heat of fusion.
Upon the second supposition, Davy remarked:
"From this experiment it is likewise evident that the increase of temperature consequent on friction cannot arise from the decomposition of the oxygen gas in contact, for ice has no attraction for oxygen. Since the increase of temperature consequent on friction cannot arise from the diminution of capacity or oxidation of the acting bodies, the only remaining supposition is, that it arises from an absolute quantity of heat added to them, which heat must be attracted from the bodies in contact. Then friction must induce some change in bodies enabling them to attract heat from the bodies in contact."
To determine, therefore, upon this last alternative, he performed the following experiment:
A block of ice, having a small channel cut around its upper edge, was placed under the receiver of an air-pump. The channel was filled with water, and upon the block, though not in contact with the water, was also placed a clock-work so contrived that one of the external wheels of its machinery came in contact with a thin metal plate. By the friction between these surfaces a considerable amount of heat could be produced, which might be made to melt wax, tallow, or any similar substance fusible at the temperature which could be thus produced.
The receiver, previously filled with carbonic-acid gas, was next exhausted as completely as possible by the air-pump and absorption by caustic potash; upon then setting the machine to work the wax was melted rapidly, and the temperature of the whole apparatus increased by more than 1° Fahr., thus proving the excitation of heat under the conditions imposed.
Consistently with the remaining supposition—the third—it was then only to be inferred that caloric had been collected from the bodies in contact. Neglecting, however, the vapor of water which formed the rarefied atmosphere within the receiver, the only other body in contact with the apparatus was the ice. But against the assumption of this latter having furnished any heat, Davy here drew attention to the water still remaining liquid in the canal, and which presumably would have been frozen had the ice parted with any heat.
It is easy to perceive that such a course of reasoning was neither exhaustive with respect to the non-existence of caloric, nor conclusive as to the dynamic character of heat. For, had he even been successful in demolishing the doctrine of caloric, the simple refutation of one physical hypothesis could never have been construed into more than an increase in probability of all those opposed to it; and in this instance, perhaps no considerations would have been accepted as conclusive by the materialists, which, failing to experimentally establish the true nature of heat, should still have left their favorite notion open to any modification, however artificial, which might reconcile it in the least degree with facts which would be doubted and distorted in the interest of these preconceived opinions.
Heat being only a particular phase of energy, it was necessary and sufficient to show, as done by Rumford, with respect to its frictional excitation, that its production depended only on the expenditure of energy—implied in its inexhaustibility—and always in the same degree, as he proved by special determinations. It was the subsequent extension of this experimental process to all modes of heat-production that constituted the great work of Joule, to be described hereafter.
But if Davy thus failed to render his experiments truly conclusive against the materiality of heat, his subsequent observations showed that individually his perceptions were most clear and definite.
Heat, ultimately, he conceived to depend upon molecular motion—calling this the repulsive motion—and to produce an effect exactly opposite to that of cohesion. The action of this motion in altering the state of aggregation, he interpreted essentially as is the custom now, and spoke of temperatures as indicating the relative quantities of repulsive motion in the same substance. He also mentioned three modes in which this motion might be increased:
"1. By the transmutation of mechanical into repulsive motion, that is, by friction or percussion. In this case the mechanical motion lost by the masses of matter in friction is the repulsive motion gained by their corpuscles.
"2. By the motion of chemical combinations of decomposition.
"3. From the communicated repulsive motion of bodies in apparent contact, that is, by conduction simply. And subsequently he generalized this statement in the dictum:"The immediate cause of the phenomena of heat, then, as Lavoisier long ago stated, is motion, and the laws of its communication are precisely the same as the laws of the communication of motion."
These essays of Rumford and Davy failed to produce, with a few rare exceptions, any perceptible effect upon the scientific opinions of their contemporaries. There would seem to have prevailed at this time a remarkable incapacity to appreciate the importance of experiments whose indications were opposed to preconceived ideas, and an antipathy to engage in unfamiliar issues; and the same distrust and indifference which so deadened the brilliance of Fresnel's immortal work in France proved quite effectual in deferring for the time the discoveries which might otherwise have followed the immediate development and experimental prosecution of this theory. Whatever interest was awakened seems to have been, for the most part, displayed in the petty, irrelevant objections, and misstatements even, brought against their methods of experiment and observed results: and the injustice of which, when not apparent, might have been easily exposed by a careful repetition or extension of these same determinations.
Dr. Thomas Young, however, in his "Lectures on Natural Philosophy," delivered at the Royal Institution, and published in 1807, assigned to them their true significance, and, reviewing much after Bacon the existing state of experience upon the question, drew forcibly attention to the superficiality of the views of those who still adopted the hypothesis of caloric.
In 1810 Haldat performed an extended series of experiments upon the heat produced by friction between various metallic surfaces. The results which he obtained were not, however, decidedly confirmatory of either supposition, but especially serve to increase our admiration for the acumen of Rumford in perceiving and stating the true law of its excitation.
The rubbing surfaces employed by him were similar in size and shape; the pressure between them was maintained nearly constant in several different experiments; but the power or energy was received in measured quantities, and from an indefinite source, namely, the pulley of a turning-lathe.
The quantities of heat developed for the same number of revolutions, or in proportionate times, were naturally, therefore, different for different metals; but as to the cause of this diversity he hazarded no positive opinion, and indeed his recorded observations do not seem susceptible of reduction to any particular theory. Had he measured the energy absorbed, or the coefficient of friction between the rubbing surfaces, he might possibly have been able to trace some relation between them and the heat produced in the operation. As it was, his observations as to difference of capacity, the influence of density, etc., were equally confused with the results, which he obtained on varying the pressure and substituting different metals; and although upon the whole his conclusions were adverse to the calorists, they were not definite enough to attract any notable attention.
In tracing thus far the inception of mechanical-heat theory, we have seen two important generalizations made: The one, fully attested by experiment, referring to the transformation of work into heat in a peculiar class of operations, and entirely independent of hypothesis, namely, that "the heat generated by friction is exactly proportional to the force with which the two surfaces are pressed together, and to the rapidity of the friction." The other, more comprehensive, including in the spirit of its enunciation thermal phenomena of every variety, and to a greater or less extent dependent on molecular and other hypothesis. These early statements are quite characteristic of, and may be used to illustrate, a subsequent division of our subject necessitated by experimental difficulties of investigation and verification.
The proposition that the entire energy existing in the universe is a magnitude as definite and unchangeable as the quantity of matter which it contains, is now considered one of the most fundamental and far-reaching in natural philosophy. The experimental evidence possessed as to the fact appears for the most part in the invariability of the ratio of any dynamic magnitude of a definite kind which disappears to that of another kind which is thereby produced, and the numerical value of which, for a particular transformation, depends only on the relative magnitude of the characteristic units as compared by the same standard system of dynamic units. That is, that the conversion of one manifestation of energy into another takes place with as great certainty and absence of waste, and with the same integrity of the elementary magnitude, as the more formal conversion of foot-pounds into kilogrammetres, or British thermal units into calorics. To the experimental establishment of this principle as involved in transformations between heat and work, and which is called the First Fundamental Law of Thermo-Dynamics, we shall return hereafter.
But in the transformation of heat into mechanical effect or work, an additional principle has been found to hold, respecting the transformable quantities of these two magnitudes as influenced by temperature, and which is known in like manner as the Second Fundamental Law of Thermo-Dynamics.
Experience has not as yet encountered any phenomena at variance with these fundamental laws; which furthermore agree with the strictest requirements of intuitive science, and illustrate, respectively, the axioms that nothing is by natural means creatable from nothing, and that things are equal to the same thing only which are equal to each other. In the development of these two principles, and the application to them of empirical laws with reference to the behavior of bodies under the action of heat or mechanical effect, consists the first principal division of the subject in which the results obtained are generally reliable.
But in assuming a complete analogy between molecular and mass energy, and in tracing the consequence of this assumption through the different forms of material aggregation, the conclusions reached are generally much beyond the present power of experimental science to explicitly confirm, and, although many of the results obtained in these investigations are of great probability, they yet are of inferior certainty to those properly included in the first division.
In short, although the laws which govern the relations of molar energy to heat are in the abstract positively known, yet in endeavoring to trace the distribution and precise condition of energy when it becomes absorbed within a body, or vice versa, the mode and minutest detail of its transformation into gross mechanical effect, the most consistent theories have heretofore depended on the hypothesis that actual or real heat is a condition of molecular kinetic energy, and that the various latent heats are due to potentialities of molecular arrangement.
The full extent to which this principle of the indestructibility of
energy had previously been recognized, or involved in the dispute as to the intimate constitution of heat, may be inferred from what has been already given of the history of heat theory. But in 1822, M. A. Seguin, in a letter to Sir J. F. W. Herschel, explicitly asserted it in support of the dynamical existence of heat, and in explanation of the work obtained from caloric in the steam-engine. The view of the subject he claimed to have derived, some years before, from his uncle, the celebrated Montgolfier.
Soon after he restated these considerations in a letter to Sir David Brewster, wherein, by a perfectly legitimate course of reasoning, and in a very lucid manner, he showed that the accepted teachings of the calorists led to a violation of this principle of the conservation of energy. For, quoting his own language:
"If we suppose, indeed, that at each stroke of the piston of a high-pressure steam-engine the quantity of caloric employed is represented exactly by the elevation of temperature of the water of condensation, abstracting all loss, it follows that we have lost nothing in obtaining a very great effect, and that, if it were possible (which is supposable) to condense the caloric contained in a mass M into another represented by x, in such a manner that it may be reduced into vapor at the primitive pressure, we may, by means of a small quantity of caloric, produce an indefinite number of oscillations."
He expressly stated, therefore, that after a mechanical effect had been produced through any given thermal agency, as in a steam engine, only that quantity of molecular motion or heat which had not been thus appropriated would remain as heat.
To him, therefore, most undeniably belongs the credit of having first publicly urged the principle of the conservation of energy against the materiality of heat, and of having considered in this connection the reverse phenomenon of the performance of work by thermal agencies.
The only indefinite or erroneous particular in his statement was that arising from the rather incautious introduction of molecular hypothesis. His leading argument was thoroughly scientific, but the oversight or neglect to refer explicitly to the disturbing effect which latent as distinguished from sensible heat might exert upon the experimental verification of his principles, served afterward as a point of attack upon the accuracy of his reasoning in general, and an opportunity, abundantly improved, to detract from his true merit as an early supporter of the mechanical theory of heat.
This criticism depends upon and applies with still greater justice to a principle which he subsequently enunciated in a work on railways, in treating of the motive-power of heat, namely:
"La force mécanique qu'apparait pendent l'abaissement de température d'un gas, comme de tout autre corps qui se dilate, est la mesure et la représentation de cette diminution de chaleur."
If in the single term "chaleur" Seguin intended to include both sensible and latent heat, his principle was undoubtedly correct; but it is to be inferred from an indicated method of determining the relative dynamical value of heat and mechanical units, that he had quite neglected to take into account any change of molecular energy other than that of sensible heat.
Nearly identical with these, though much more celebrated, were the subsequent speculations of Dr. J. R. Mayer upon this subject. In a memoir published in Liebig's Annalen, for May, 1842, entitled "Bemerkungen über die Kräfte der neubelebten Natur," he undertook to answer the questions: "What are we to understand by force? and how are different forces related to each other?" Toward the latter part of the disquisition he entered upon the subject of the mutual convertibility of heat and mechanical energy, considering the generation of heat by the shock or gradual stopping of a falling body, by friction, and by compression; and illustrating by the heat excited in the bearings and rubbing surfaces of water-mills and railway-trains; and by the diminution of the earth's bulk in the falling of a body to the ground.
In this he first expressly used the term equivalent, in speaking of the relation of heat, to mechanical effect; and by the same method as that employed in the deduction of Seguin's value, though with more accurate data, found the distance through which any mass of water would have to fall, in order that its temperature, by the shock of sudden stoppage, might be raised from 0° to 1° Cent., to be 365 metres.
The physical reasoning upon which he founded this determination was manifestly incomplete, if not erroneous; and, on this account, his claims as an original promoter of correct theory have been made of late the subject of considerable dispute. In view of the historical importance attaching to this point, and because an allowable explanation of the phenomenon referred to will illustrate very fully the received distinction between sensible and latent heat, we here make a slight digression to consider more particularly the thermal effect attending the compression of elastic fluids.
The term specific heat is ordinarily employed to designate that quantity which it is necessary to impart to unity of weight of any specified substance, in order that its temperature may be raised by one degree; no discontinuous change of physical state occurring. A part of this heat, it is thought, is used in raising the temperature of the substance, and thus increasing the real heat or thermal contrast of the body; while the remainder is expended in producing, as it were, some change in the potentiality of intermolecular distance, or molecular motions, not indicated by the thermometer, but in general attended by the expansion or contraction of the body heated. The energy existing in this latter form, and measured in heat-units, has been called by Clausius the ergonal content of the body.
If we were, therefore, to suppose the following effects produced, in a specified manner, during the reception of a quantity of heat by any portion of an elastic fluid, namely, an increase of temperature, a change in the mean distance or motions of the molecules not causing any variation of temperature and a performance of external work by the consequent increase of volume against exterior resistance, it is evident that we could not consider any one of these effects to be the dynamical equivalent of the whole acquisition of heat. Much criticism upon the original reasoning of Mayer has therefore been called forth by this fact, that, without proving the absence of the second effect above mentioned, or in any way referring to the possibility of its disturbing influence upon the calculation, he arbitrarily assumed that the mechanical energy expended in compressing atmospheric air should be regarded as the mechanical equivalent of the heat thus rendered sensible.
But though erroneous in principle, this method of determining the mechanical equivalent of heat was afterward shown by Joule to involve no sensible inaccuracy of result in the case of air and other permanent gases.
The experiment by which this conclusion was attained consisted in the repetition, with a slight but very important modification, of one originally designed by Gay-Lussac to investigate the effect upon the temperature of a gas of its free expansion into a vacuum.
The apparatus consisted of two reservoirs, R and E, which might be joined by connecting-tubes and a coupling-nut, and each closed independently by a very perfect stopcock. Into one of these dry atmospheric air was forced until a tension of about twenty-two atmospheres at the ordinary temperature of the room was attained. The other was exhausted by an air-pump. Being then coupled together, they were immersed in a tank containing about sixteen and a half pounds of water, which was stirred, and its temperature taken on a very sensible thermometer, indicating approximately thousandths of a degree. The stopcocks were next opened and the air allowed to rush from one reservoir to the other until the tensions were more nearly or quite equal in both. Lastly, the water was again stirred and its temperature carefully noted. A correction was obtained after each experiment, by noting the increase of temperature caused by an equal amount of stirring, uninfluenced by any possible effects of the expansion.
Five experiments upon the thermal effect thus attending the expansion of atmospheric air showed a mean increase in the temperature of the water of 0.0074°, while the correction to be applied amounted to 0.0068, leaving a difference quite within the limits of observation by this method. Joule, therefore, concluded that "no change of temperature occurs when air is allowed to expand in such a manner as not to develop mechanical power."
If this result or property of atmospheric air had been known to Mayer, and construed by him to imply the total absence of a transformable, internal store of potential energy in gaseous substance, so that the energy embodying the condition variously styled its pure, real, actual, or sensible heat could only be affected by some external agency, mechanical or thermal, and if the effect upon a thermometer, produced by this condition, had been also known to vary directly with the whole quantity of energy comprising it, the method which he indicated would have led to an admissible result.
But, in reality, Gay-Lussac, from his original experiments, had not come to any very definite conclusions on this point. The temperature of each receiver had been found by him to change; but not using an equivalent device to that of the submerging tank of water, he had not been able to determine, on the whole, whether heat had been lost, or gained, in the expansion. When, therefore, Mayer, in 1849, defended his claims by a reference to these first experiments on this point, the answer was available to Joule that, prior to his own researches, the all-important principle assumed had not been recognized in science; and that the results obtained by Gay-Lussac tended only to render the question still more doubtful.