(10.) A rod composed of a mixture of tin and bismuth in equal portions, which melts at the temperature of boiling water, was plunged at one extremity into a basin of mercury. The mercury was kept successively for a long time at different constant temperatures, by means of a lamp placed below it. A thermometer was adjusted to the other extremity of the rod, in a little capsule filled with mercury. Observations of the temperature indicated by this thermometer, corresponding with each stated temperature of the mercury in the basin, were made, when the state had become stationary. The following table exhibits the corresponding excesses of temperature of the mercury and of the thermometer above that of the air. The latter was 20°.

Before we compare this table with theory, it is right that we express our belief that there has been some mistake in the observations. We think this will be made out when it is seen that the following is the order of elevations of the upper thermometer, due to elevations of temperature of the heated end. For the first 10°.25 the thermometer rose 3°;

For the second 9°5 the thermometer rose 2°.5;
9°.5 the thermometer rose 2°.5;

For the third

in which the rise of the thermometer is nearly, but not quite, proportionate to that of the mercury; but

For the fourth 19°5 the thermometer rose only 2°.5.

This we think very unlikely. We should expect to find the proportion of the increase of temperature of the thermometer to that of the mercury continually diminish as the absolute temperature increases. The following are, however, the ratios as given by the above table:

M. Biot gives the following results as calculated by an empirical formula:

II. and III. On Libri's or Poisson's hypothesis we have approximately (from 12 and 13) v Cu D u2.

=

If we apply experiments (3.) and (5.) to obtain the constants C and D, there results

It must be observed here, that we have only one constant to be determined by experiment. We must not expect, therefore, to find so close an agreement as when we have two.

We are not ignorant that there are a vast number of experiments on radiation and conduction to which we have not referred. Our reason for omitting the mention of some of the most valuable is, that we desire to confine our attention strictly to the matter in hand-the examination of theoretical formulæ by experiments calculated to test their accuracy.

III. We hasten, then, to the third part of our Report. We propose very briefly to reflect on the consequences deducible from the computations we have entered into; and to conclude by adding a few remarks tending to suggest the proper mode of conducting experiments which shall serve a better purpose in effecting the object of establishing theory. We may observe then, 1st, that experiments on the permanent state of temperature at different points of a long bar of a good conducting substance, and which radiates into air, are utterly valueless in this matter. To prove this, we will write down the difference between the calculated and observed values of the temperature for a few cases.

It is altogether impossible to decide which is the best formula from these results. Apparently Formula I. is as good as any of them, and yet we are sure, à priori, that it is absolutely erroneous. The ratios of the error to the whole temperature when greatest are, for the different formulæ,

I. 49, II. •465, III. •458,

IV. 272.

These ratios are very considerable, and as they all arise at the point of greatest distance from the heated extremity, they prove clearly enough that the effect due to the presence of the air is far greater than that which arises from the difference of radiation between Newton's law and the law of nature. But even if experiments of this kind were made in a vacuum, it is probable that the law of change would be found to remain so uniform as to admit of its being represented by either of the equations resulting from the second, third, or fourth hypothesis. Nor will our conclusions be more satisfactory on referring to M. Despretz's experiments. Let us write down the errors in

The maximum ratios of the error to the whole temperature are

I. .42, II. .36, III. 37, IV. 28.

We must remark again, that this experiment, as contrasted with the foregoing, presents us with most anomalous results. Both were made on a bar of iron; the temperature of the surrounding air was nearly the same in both; the extreme temperatures of the former lie beyond those of the latter on each side; and yet the former verifies, or nearly so, all the formulæ,-the latter disproves them all. We trust neither; nor do we think the difference can be attributed to the coating with which the iron was furnished in the second experiment, although that might produce some effect. We feel, therefore,

utterly unable to draw any conclusion from these experiments. We shall experience the same difficulty if we proceed to examine the other results in the same way. If we confined our attention to experiments (1.), (2.) and (3.), we might conclude that all the formulæ are correct; if to (8.) and (9.), we should certainly conclude that all are incorrect. Nor is it easy to say which is the best from the former test, or which is the worst from the latter. Seeing, then, that agreement with experiment is no test of truth, it is not too much to argue that disagreement is no test of error. We must eliminate the effect of the air, or be provided with experiments in vacuo, before we can form our conclusions, unless we can be furnished with experiments of a much more searching character than these.

2. It is hardly necessary to call attention to the insufficiency of the class of experiments which was made by M. Fourier, and of which we have exhibited one specimen. The results for the ring, it is true, are not so obvious that they might be deduced from popular reasoning, and we must give M. Fourier great credit for selecting these results in order to show the agreement of his theory with experiment; but as we are now in want of a means of disproving rather than of establishing theories, we must look for results of a totally different character. We shall point out where such are to be found by and by.

3. We think we may consider that experiment (10.) shows the inaccuracy of the first formula; it fails, however, to give any preference to one of the other three. The table of errors is as follows:

The maximum ratio of error to the whole temperature is

It is needless to comment on these results. None of them are sufficiently close to warrant any favourable conclusion, and the first is so wide, that, were there no other reasons, we should on this account be disposed to reject the corresponding formula, and with it the axioms on which it depends.

We do not know that any other remarks are called for by a review of the results of theory as contrasted with experiment. What, then, does the whole amount to? We find that there are three distinct ways of theorizing, each adopted, apparently, in accordance with the known laws of nature, but which differ essentially from each other. We do not perceive that our existing experiments bear with greater weight in establishing or in disproving any one of them than it does in establishing or disproving the other two. Each is confirmed by one experiment, each at variance with another. Are we to account for this circumstance from the difficulty of conducting the requisite experiments, or are we not rather to attribute the anomaly to the little regard which has of late years been paid to a certain class of subjects, and especially to the one before us? We are not aware that it has suggested itself to any one experimental philosopher to examine into the laws of conduction. Much labour, it is true, has been bestowed in examining the conductive powers of different substances, and to the results of experiments carried on with this object we naturally look with the hope of extracting a law; but, unfortunately, the nature of the experiments we are presented with is not such as

will lead to what we seek. They were not originally conducted with reference to the state of things assumed to exist in theory, and are, in consequence, of less value when allowance is made for the difference between what they express and what theory requires. Now we do not deny that difficulties do attend the experimental examination of this subject, when it is intended to make everything correspond with the state supposed in theory. The chief and greatest of these we conceive to arise from the presence of the air. MM. Dulong and Petit have shown that the quantity of beat carried off by the air is not only very large, but is governed by a law very different from that of ordinary radiation. Means have therefore to be devised for removing this cause of error; but we are far from thinking that the difficulty of effecting this amounts to an impossibility. If MM. Dulong and Petit could succeed in determining the rates of cooling of a body in vacuo, we cannot see why others should not succeed in observing the stationary temperature at one point, at least, of a body which radiates in vacuo. This leads us to the suggestions with which we shall conclude the present Report. We shall offer two: 1st, as to the most important experiments; 2ndly, as to the mode by which they may be conducted.

It is perhaps chargeable against the theoretical writers on this branch of physics, and especially against M. Poisson, that they have not presented their results in a form sufficiently tangible to direct or suggest the application of experiment to them. It is much to be regretted that no attempt has been made to obviate this. With the view of remedying the state of things to a certain extent, we have exhibited in their most simple forms some of the more obvious conclusions to which the different theories lead. No doubt much might be done in this way, but, until called for by the entry of experimenters on the field, a large and varied collection of formulæ would serve no useful purpose. One class of experiments alone appears amply to suffice for our present purpose. The object being, to discover a law of conduction, it will be best attained by the selection of circumstances in which radiation either plays no part at all, or in which its effect is very simple and readily eliminated. The former condition exists in the problem which is solved by formulæ 1, 15 and 16. By selecting a substance of small conducting power, such as marble, and coating the block with a substance which will radiate very slowly, this experiment may be made on a block of no very great dimensions. For many reasons this experiment is well worth trying. It will probably distinguish at once between the three theories. It will certainly offer strong reasons for rejecting either the third or the fourth. Of course it will hardly serve to establish directly either of them. To effect this, we would point out another most important experiment,-The determination of the state of temperature at one extremity of a bar which is heated at the other extremity. This experiment should be made on a variety of bars, of different conducting powers and of different lengths. With a set of careful experiments of this nature, we believe we could pronounce, without fear, the true law of conduction. Nor do we think the difficulties attendant on the con duct of the experiments to be at all insuperable. The greatest obstacle is, no doubt, the expense of apparatus; but where we find expense overruled in the prosecution of experimental researches into less important and certainly not more interesting branches of physics, where theory has hardly opened a field for speculation, and where curiosity alone prompts the inquiry, it must excite our surprise that so little has been done in this case, which presents analytical developments of great beauty, and, independently of its close connexion with the favourite theories of light and the discoveries of chemistry, deserves to rauk high amongst the physico-mathematical sciences. But,

leaving expense out of the question, the real practical obstacle is the presence of the air. We have seen that the law of cooling into air is different from that of radiation. Even supposing, therefore, we were in possession of the correct statement of that law, such would be the difficulty of obtaining formulæ from it, that to attempt to eliminate its effect, together with that of radiation, is almost hopeless. If it can be done at all, it must be by means of experiments carried on in air of different elasticities. It has been proved by MM. Dulong and Petit, that "the velocity of cooling of a body due to the sole contact in a gas, depends, for the same excess of temperature, on the density and temperature of the gas; but this dependence is such that the velocity of cooling remains the same if the density and the temperature of the gas change in such a way that the elasticity remains constant." The effect, then, of the presence of the air is to introduce a term which involves a power of the elasticity as one factor, and a function of the excess of temperature as another. The latter function may be determined (perhaps) by means of a number of experiments made at different elasticities. But we should greatly prefer a set of experiments on radiation in vacuo. It appears to us, that the difficulty in this case is very much the same as that against which MM. Dulong and Petit had to contend in investigating the kindred law of radiation; and we should conceive that a similar contrivance to that which they used might be adopted to overcome it. All that we require is, that a certain portion of a bar heated at one extremity, radiate in vacuo, and that the temperature at two of its points, the other extremity being one, be capable of constant observation. MM. Dulong and Petit made use of a copper balloon which could be exhausted of air, and by means of ice be kept constantly to the freezing temperature, notwithstanding the radiation of the heat from the body within it. A somewhat similar contrivance we conceive would serve for the conduct of the experiment before us. The bar of metal to be experimented on might pass through the balloon and be heated in air, whilst the assumed point of heating might be marked by a thermometer inserted into a hole in the bar just within the balloon. We wish M. Biot had marked his lowest point, not at the surface of the heated mercury, but at a point a little above it; it would have insured greater steadiness in the results. Should any one think of undertaking this experiment, we would recommend that he extend his observations over a wider range of temperatures than M. Biot has done. The thermometer which represents the heated end of the bar should stand permanently at every 5°, from 0° to as high as can be accomplished. It must be borne in mind, that two at least of the observations are requisite for the determination of the constants, except in the case of formula 14. The observations should likewise embrace a succession of bars of different substances, iron, brass, lead, etc., all of the same dimensions. Different series of observations should be made, in which the dimensions of the bars have different constant magnitudes, and others in which they have different lengths. All the substances might be coated with the same varnish, so as to render their radiating powers the same. With such experiments, we have no doubt that the law of conduction, although not like the law of radiation, an inference from direct observation, might be readily established, and the science of heat placed on the same footing with the other mathematical sciences. We hope that the Association, in making known the wants of this branch of philosophy, will induce some of the numerous distinguished experimental philosophers whose names appear on their list, to take an interest in this matter.

P. KELLAND.