From George Gabriel Stokes   7th May 1861

Lensfield Cottage Cambridge | 7^th May 1861

My dear D^r Tyndall,

Your paper¹ was ordered to be printed last Thursday. I directed M^r White² to get estimates for the plate so that we may be getting on with the plate. I have got the MS which I took partly to help me in making some remarks from the referees³ and partly to save expense in case you should wish to make any more than a few trifling changes which could be made on the proof sheets.

I was one of the referees, and I have the following remarks to make

I.

It does not seem to me that there is any real discrepancy between Franz⁴ and yourself at least nothing more than is fairly attributable to the difference in the sources of heat and similar differences in the mode of conducting the experiments. Franz says nothing about drying the air and other gases except in the case of nitrous acid gas which as ordinarily produced is liable to be charged with water and in which after all the drying was so imperfect that Franz speaks of the interior of the tube being moistened by it. He doubtless took for granted that the small quantity of moisture present would go for nothing. You on the other hand have discovered that while dry air is very transparent watery vapour is highly absorbent. Hence Franz’s results for air should be compared, not with yours for dry air, but with yours for the air of the laboratory, and the amount of absorptions which you both make out, though not equal, are quite comparable with each other.

On the other hand I cannot imagine that the cause you suggest can have materially affected Franz’s experiments. He appears to have taken a series of observations in which a screen was alternately interposed and removed; and as this occupied some time any such merely temporary cause of disturbance as that you mention could hardly fail to be detected by the irregularity which it would produce in the results.

II.

p.15 [Explanation of the apparent (but temporary) decrease of absorption when the air was exhausted] “due to the aqueous vapour precipitated” .

I don’t suppose the result depends upon the precipitation of vapour, (though probably some was precipitated) but upon the high emissive power of water as compared with air. The absorbing and emitting power of water is likely to be much the same in the elastic and in the liquid state, so that the same effect I imagine would have been produced (making allowance for the smaller quantity of water present) had the quantity present been too small for any to be precipitated. Indeed precipitation, as far as it goes, seems likely to produce an antagonistic effect, on account of the latent heat given out.

III.

P. 16 end: “so that the heat emitted by the copper plate might cross a vacuum before entering the experimental tube, thus retaining the quality which belonged to it at the moment of emission”. Add except in so far as it might be interfered with by the absorption of heat by the rock salt” otherwise the statement is too absolute.⁵

IV.

The only serious point I have to remark about⁶ is the connexion or supposed connexion between good conduction and bad radiation, bad conduction and good radiation.

Now in the first place is it a physical law that good conductors are bad radiators and bad conductors good radiators? I confess I doubt it. It is true the metals conduct well and (at least when polished) radiate badly. But the metals are linked together by so many physical and chemical properties that the different metals must not be looked on as so many independent witnesses. And what do you say to charcoal (graphite) Being black it is almost certainly a good radiator, better I should suppose than white porcelain. But as it conducts electricity pretty well it probably also conducts heat well.

In focusing the electric light for a short time only with a graphite pole I have been struck with the high temperature of the graphite at the end remote from the seat of incandescence. A vitreous substance would not have become sensibly hot in the time so far from the seat of the high temperature.

And now for the reasoning. This seems to me to assume that a given molecule loses the main part of its motion in the course of one or two vibrations. For you suppose that in the case of a good radiator a molecule does not lose much motion by communication to the adjacent molecules because it has already lost it by communication to the ether, which acts as a buffer. This I cannot understand except on the condition I mentioned. But if the fraction of the vis viva of a molecule which is lost in a single vibration is very small, so that a number of successive vibrations are nearly equal, it seems to me that the loss by communication to the ether and the loss by communication to other molecules must take place sensibly independently of each other. For what happens in the course of a single complete vibration must decide whether the communication in either way shall be comparatively rapid or not.

Now the phenomena of interference, in which one undulation is found to interfere with another which precedes or succeeds it by a great number of periods. (Fizeau and Foucault have traced interference up to a retardation of somewhere about a couple thousand undulations.⁷ This seems to show that in the cause exciting these undulations there must be great regularity, that the motion of a vibrating molecule must be sensibly the same for a great number of consecutive vibrations so that only a very small fraction of the motion can be lost in one vibration. But if so it seems to me that the loss by communication to the adjacent molecules (conduction) and the loss by communication to the ether (internal radiation) must go on sensibly independently of each other; so that if the amplitude of excursion were diminished in the ratio of 1 to $1-c$ by the first alone and 1 to $1-r$ by the 2^nd alone, in one vibration, c and r being very small fractions it would be diminished in the ratio of 1 to $\overline{1-c}$$\overline{1-r}$ by both together or in n vibrations in the ratio of 1 to ${(1-c)}^n$ ${(1-r)}^n$ and I can see no reason why a diminution of c should imply an increase of r or the converse.

V.

p. 82 “A lead bullet suspended from a string and made to oscillate will do so more quickly than &c” more or less quickly according to circumstances.⁸ Thus if two bullets were joined so that the line joining the centres was in the direction of oscillation they would oscillate more quickly than a single sphere.

But the time of oscillation of a lead bullet oscillating as a pendulum would be increased by the resistance of the water (supposed for simplicity to be perfectly smooth) only in the proportion of $\sqrt{s}$ to $\sqrt{s+\frac{1}{2}}$ (s being the specific gravity of lead, about $\mathrm{\text{11}}\frac{1}{2}$) or 1 to $1+\frac{1}{4s}$ nearly or 1 to $1+\frac{1}{\mathrm{\text{46}}}$. The effect on the time would be less and less in proportion to the lightness of the fluid—compared with the solid. Now taking account of the small inertia which we must attribute to the ether and the persistence of the luminous vibrations of ponderable molecules I don’t think the time of vibrations can be sensibly affected by the greater resistance.

Supposing the vibration to be sufficiently broadly based I should prefer regarding the slow vibrations and the greater resistance to distinct consequences of a common cause (the greater size and unwieldiness) to supposing the latter to be the cause of the former.

As to Sir W. H’s paper⁹ next Thursday (tomorrow) is Ascension Day; 16^th Croonian Lecture¹⁰ 23^rd Whitsun week no meeting 30^th virtually promised to Dr Smith.¹¹ I am afraid therefore I cannot have time for the proof while he is in Town.

The other referee has also made remarks about which I have written to him.

Yours very truly | G.G. Stokes

D^r Tyndall F.R.S.

RI MS JT/1/S/221

RI MS JT/1/TYP/4/1365–9