[page] 187

A. R. Wallace took a different view as to what Galton had achieved in a letter of the following spring.

THE DELL, GRAYS, ESSEX. March 3rd, 1876.

DEAR MR GALTON, I return your paper signed. It is an excellent proposal. I must take the opportunity of mentioning how immensely I was pleased and interested with your last papers in the Anthrop. Journal. Your 'Theory of Heredity' seems to me most ingenious and a decided improvement on Darwin's, as it gets over some of the great difficulties of the cumbrousness of his Pangenesis. Your paper on Twins is also wondrously suggestive.

Believe me, Yours very faithfully, ALFRED R. WALLACE.

F. GALTON, Esq.

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Meanwhile besides the criticisms already referred to, there were factors, other than the hope of peace, inducing Galton to enlarge his Committee and widen its programme. As early as February 3, 1891, Alfred Russel Wallace had written to Galton urging that the time was ripe for an experimental farm or institute to undertake researches which might decide disputed points in organic evolution.

Copy of Letter from Alfred Russel Wallace to Francis Galton†

PARKSTONE, DORSET. February 3, 1891.

MY DEAR MR GALTON, Don't you think the time has come for some combined and systematic effort to carry out experiments for the purpose of deciding the two great fundamental but disputed points in organic evolution,—

(1) Whether individually acquired external characters are inherited, and thus form an important factor in the evolution of species,—or whether as you & Weismann argue, and as many of us now believe, they are not so, & we are thus left to depend almost wholly on variation & natural selection.

(2) What is the amount and character of the sterility that arises when closely allied but permanently distinct species are crossed, and then "hybrid" offspring bred together. Whether the amount of infertility differs between the hybrids of species that have presumably arisen in the same area, & those which seem to have arisen in very distinct or distant areas—as oceanic or other islands.

* The Royal Society had on Dec. 11, 1896, decided to retain the old name of the Committee, which contained the word "measurement." It was not till the following year, that with enlarged numbers and a wider programme, the Council acceded to Galton's request that the Committee be called "The Evolution (Plants and Animals) Committee."

† I have to thank Alfred Russel Wallace's son, Mr W. G. Wallace, for kindly permitting me to publish the following letters of his father.

[page] 129

Both these questions can be settled by experiments systematically carried on for ten or twenty years. The question is how is it to be done. Talking over the matter with Mr Theo, D. A. Cockerell, a very acute & thoughtful young naturalist, we came to the conclusion that a committee of the British Association would probably be the best mode of carrying out the experiments, by the aid of a B, Ass illegible . grant & a Royal Society grant, aided perhaps by subscriptions from wealthy naturalists. It seems to me that one paid observer giving his whole time to the work could carry out a number of distinct series of experiments at the same time,—and if the Zool. Soc. would allow some of the experiments to be made with their animals in their gardens much expense would be saved. To be really good however the hybridity experiments (and the others too) would have to be carried out with large numbers of animals, and thus some sort of small experimental farm would be required. Surely some wealthy landlord may be found to give a small tenantless farm for such a purpose. Then, using small animals such as Lepus and Mus among mammalia, some gallinaceous birds and ducks, and also insects, a good deal could be done even on a large scale, at a small cost. On the same farm a corresponding set of plant-experiments could be carried out; and an intelligent well educated gardener or bailiff, with a couple of men, or even one, under him, could superintend the whole operations under the written directions and constant supervision of the Committee.

Would you move for such a Committee at the next B. Ass2. Meeting? You are the man to do it both as the original starter of the theory of non-inheritance of acquired variations, the only experimenter on pangenesis, & the man who has done most in experiment and resulting theory on allied subjects.

We thought first of a separate Society, but I doubt if a new society could be established & supported, whereas a Committee either of the B. Ass illegible , or of the Royal Society could do the work quite as effectively & would probably receive as much support from persons interested in these problems. It seems to me a sad thing that years should pass away & nothing of this kind be systematically done. I feel sure you would meet with general support if you would propose the enquiry. Believe me, Yours very faithfully, ALFRED R. WALLACE.

FRANCIS GALTON, F.R.S.

P.S. It would of course be better still if a fund could be raised sufficient to establish an Institute for experimental Enquiry into the fundamental Data of Biology. This is surely of far higher importance than the anatomical, embryological, & other work for which the Plymouth Biological Station was founded.

A. R. W.

42, RUTLAND GATE, S. W. Feb. 5/91.

MY DEAR MR WALLACE, The views you express so clearly & forcibly, agree with those I have often considered—ranging between a modest cottage with hutches & a bit of ground, up to an Heredity Institute. There was also a half move in this direction made last spring by Ray Lankester, Romanes & others. The difficulties I fear and which I hope you can remove, are as follows. Let us suppose that funds have been collected, a small farm procured and a sensible manager installed in it and that operations are ready to begin. Also I would suppose that the cost of conducting experiments would be met by those who devised them, who themselves had obtained a grant for the purpose from the R. Soc., Brit. Assoc. or otherwise.

Now (1) I doubt if it would be easy to devise a sufficiency of experiments to occupy the establishment of a sort that wd. generally be recognised as crucial. In the two groups of desiderata you mention, no one that I know of, has yet suggested an experiment, much less several experiments, that those who believe in and those who don't believe in the hereditary transmission of acquired characters would accept as fair. If a few such could be devised all my fears as to the utility of the establishment would vanish. If it could settle this one question pains and cost would be amply repaid.

(2) Similarly as regards the sterility question though in a much less degree. The uncertain and often large effects of confinement on fecundity would be a serious disturbing cause.

It then seems to be the first desideratum before making any move that a fairly long list of definite problems, that such an establishment might be set to work upon, ought to be drawn up. Would you put your views as to these on paper!

The number of experimentors is sadly small.

P O III

17

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(3) Another difficulty is that the experiments are not likely to be so carefully tended & guarded in an establishment as they would be by oneself or by personal friends. I have had some very marked evidence of this in my own experience, which I don't like to put on paper for fear of causing annoyance.

If the difficulties I have mentioned can be shown to be small, all the rest would be plain sailing. The farm would bear a similar relation to Heredity both plant and animal that the Kew Observatory does to experimenters in Physical Science.

It might grow into a repository of stud books and all about domestic animal breeding, and pay its way well in this department. Also it might become a repository of family genealogies & facts about human heredity, and also pay its way here; the people love to have their genealogies put on record, photos of family portraits preserved, &c. & would pay for the trouble it might cost to keep them.

But the first thing is the experimental farm—in connection with Kew or Chiswick—the Zool. Society & Marine biological laboratories. It could be started moderately under the same roof, so to speak, as one of these, so as to avoid many expenses of a separate establishment, while an independent home was being prepared for it to be entered into if it succeeded.

I have much that would be helpful to say, if you can remove these initial difficulties of prospect. Very sincerely yours, FRANCIS GALTON.

Pray give our united kind remembrances to Mrs Wallace, & accept them yourself.

Copy of Letter from Alfred R. Wallace to Francis Galton.

PARKSTONE, DORSET. Feby. 7th, 1891

MY DEAR MR GALTON, On receipt of your interesting letter I sat down & jotted the enclosed notes of the kind of experiments that it seems to me would test the theory of heredity or non-heredity of individually-acquired characters. Also a few as to fertility or sterility of hybrids, amp; as to the real nature of some of the supposed instincts of the higher animals. I do not myself see much difficulty in carrying out any of these, but then I am not an experimenter as you are. Still, I shall be glad to know exactly where the difficulty or insufficiency lies. If these, or any modifications of them, would be valuable & to the point, it seems to me that the mere keeping the plants and animals in health & properly isolated would fully occupy the keeper or keepers of the farm,—while the actual experiments—the deciding on the separation without selection of the various lots to experiment with,—which should be crossed & when, and other such matters, would recur only at considerable intervals & could be supervised by the members of the Committee, or some of them, by means of, say, a weekly inspection.

I have limited my notes to three points in which I feel most interest, but of course experiments in variation such as Mr Merrifield is carrying on for you, could be added to any extent if there were any danger of the keepers having too little to do!

All the experiments I suggest would require considerable numbers of individuals to be kept healthy and to be largely increased by breeding,—and they would all have to be continued during several years depending on the duration of life of the various species experimented with.

My wife and I are in pretty good health & beg to be kindly remembered to Mrs Galton. As everybody seems to come to Bournemouth we shall hope some day to have a call from you.

Yours very faithfully, ALFRED R. WALLACE.

F. GALTON, Esq., F.R.S.

This letter was accompanied by a detailed list of possible experiments.

42, RUTLAND GATE, S. W. Feb. 12/91.

MY DEAR MR WALLACE, I have thought much & repeatedly over your letter & have talked with Herbert Spencer & with Thiselton-Dyer, but cannot yet see my way. I hate destructive criticism,—for it is so easy to raise objections,—& want to offer constructive criticism & to help progress but have every point in view & in all the details I see serious difficulty without any considerable gain.

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As an example of many others of the suggested experiments, take the first, viz. that of plants in windy & in still localities. Suppose (1) there was a difference in the seedlings from them, then the advocates of non-inheritance of acquired faculties would protest against its applicability saying that there had been selection, the lofty plants & the wide spreading ones would have been preferentially blown down and the weakly ones would have been killed by the rigour of conditions, therefore there had been selection in favour of the small & hardy. Now suppose (2) that there was no difference,—then the same people would say "I told you so." The expt would be for them a case of "heads you lose, tails I win."

Next, to produce any notable effect the expt must, as agreed by all, be protracted for many generations.

Lastly, nature affords an abundance of excellent examples, far superior to artificial ones. Thus take an (elevated) region swept with winds but with hollows in it which are sheltered and all of which is forest clad. The trees in the sheltered hollows will have been from time immemorial finer than those of the same kinds of the exposed places; collect the seeds and plant them under like conditions elsewhere.

During a (Swiss) tour a man might collect an abundance of such seeds of contrasted origin of many species of trees. Even a morning's walk would afford more data than a century of artificial experiment.

So again the seeds of plants originally of English stock but reared for some generations in various parts of the world might be collected and planted side by side.

[The last is Thiselton-Dyer's proposal.]

The only certain employment in the plant department of your proposed farm is to make experiments such as these, or rather to verify in a regular methodical way much that is known already, including expts on the opposite side such as graft-hybridism.

Dyer says that no experimental work is likely to succeed at such places as Kew in the ordinary course of work, where careful oversight is required. The men have much other work to do. It would require a man to be specially devoted to its oversight.

The animal experiments seem to be enormously costly.

The case you mention of hybrids & sterility would require many hundreds of animals at the lowest of the computations you give data for. Where the effects of disuse are concerned the animals should be, as a rule, underfed as regards their appetites and only eat just enough to keep them in health; then as there is a deficiency of material for growth, economy of structure would be effective. This would be very difficult to ensure. Some of the most interesting experiments are those of the Brown-Sèquard type, but these must be put out of court in the present mood of the public & of the law.

Is not the bird nesting experiment continually the unconscious subject of experiment in those fowls who have been hatched from eggs in incubators?

Did you happen to see some remarks I made at Newcastle British Assoc/n, which are printed in the last Journal but one?

I suggested expts on those creatures which are reared from eggs apart from parents. Chickens in incubators, fish, & insects. The incubator industry is large in France & so is the silk-worm. But the naturalists present seemed not inclined to dwell on those views*.

Could anything be made of the following:
A farm for the verification of easy experiments, within easy reach of London.
Cordial relations between it and
(1). The Zoo, the Horticult., Kew, & Royal Agricult. Society.
(2). Private persons of various ranks who would agree to help in expts.
Library of reference on heredity got mostly by begging.
Log-book of daily work preserved (? in duplicate).
Publication of results in some one of the existing Scientific periodicals.
Superintendent (qualifications & Salary to be considered).
All under a c/ttee (? of the Royal Society).
In all this I am keeping the Kew Observatory in view as a somewhat analogous institution.

But before anything could be done, even before asking for its serious consideration, a few carefully and fully worked out proposals of experiment ought I think to be drawn up. I mean just as much as would have been done if the proposer handed them in to the Gov/t Grant or other committee, for a grant of money.

Very sincerely yours, FRANCIS GALTON.

* See our p. 57 above.

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Copy of Letter from Alfred R. Wallace to Francis Galton.

PARKSTONE, DORSET. Feby. 13th, 1891.

MY DEAR MR GALTON, It will be I am afraid impossible to discuss the difficulties of experiment you urge by correspondence, and I will therefore confine myself to a short reply to the objections you have actually made, which seems to me very easily done.

Plants in windy and still air.

You say, "it might be said" there had been selection. But this is very easily obviated, & is the very point on which experiment is superior to observation of nature. In an ordinary open garden or field plants properly cultivated are not killed or prevented from flowering & seeding by wind. They grow healthily under it, and I feel sure that not one in a hundred plants would so suffer. The contrast wd. be produced not by the violence of the wind in the one case but by its absence in the other set, they having grown in a glass-covered (or glass-sided) garden. If a common perennial plant was grown—a mallow or a wallflower—for example—a set of 50 or 100 plants might be grown on for 3 or 4 years so as fully to establish whatever change could be produced in the individuals by the diverse conditions. Then at the end of that time take the whole of the seed produced by each lot,—take two samples of say the 100 smallest or lightest or better perhaps 100 of the average of each, and cultivate them side by side under identical conditions. It would not matter to me, or I think to you, what anybody said, but if there were—(a) a decided & measurable difference in the two lots of plants from which the seeds were taken, and—(b) there was no measurable or decided difference between the plants grown from these seeds under identical conditions, this would be one definite fact against inheritance*,—while if there was a difference of the same nature & fairly comparable in amount it would be a decided fact in favour of inheritance. No doubt it might be urged that the effect would be minute but cumulative, & that might be admitted, & the experiment continued under exactly the same conditions for say ten generations. If then no differential effect were produced in the offspring the evidence would be strong against inheritance. Of course the fairest way would be for the advocates of inheritance to formulate the experiments they would admit to have weight, and the opponents of inheritance to do the same.

Then you say "nature affords an abundance of excellent examples, far superior to artificial ones." This I altogether demur to. In nature we always & inevitably have selection of various kinds, due to soil, aspect, winds, enemies, overcrowding, &c. &c. &c. & we cannot possibly separate the effects of these from any possible inherited effects due to diversity of conditions. But this is what we can & do do in cultivation.—We save plants from overcrowding & therefore from the struggle with other plants, we can give all the same soil & aspect, protect all alike from enemies, give both the same selection or the same absence of selection of seeds. In nature you cannot possibly tell whether any peculiarity in individuals is due to conditions or to genetic variation, while if you take those cases where the difference is clearly in adaptation to conditions—as the dwarfer plants at higher altitudes—you have the probability, almost certainly, of a considerable amount of nat. selectn. By experiment you are able to avoid all these uncertainties & determine the effects of certain definite modifications of environment on individuals,—& then ascertain whether the modifications thus produced are inherited.

In nature too, you have the uncertainty introduced by double parentage; each parent in all cross-fertilised plants, may have had different characters & have grown under different conditions. In experiment you eliminate this cause of uncertainty.

Of course the experiments with animals would involve expense, but with the smaller animals not very much,—& I understood you to say that this would not be an obstacle.

If you or any one else will point out the difficulties or uncertainties in the other experiments I suggested I will be glad to answer them, as I think I have done in the one case you have referred to.

It is only in this way that we can arrive at a satisfactory mode of procedure, & I regret that I cannot have the advantage of discussing the question with yourself & others who are well acquainted with the subject and with the special difficulties of experimentation.

Believe me, yours very truly, ALFRED R. WALLACE.

* [i.e. of acquired characters.]

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P.S. Pray do not trouble to reply to this unless you think anything further from me may be of any use.

A. R. W.

Of course I have referred to the one experiment of wind & no wind as an example, not by any means considering it one of the best experiments.

A. R. W.

It will be seen that Wallace had a due appreciation of the necessity for "large numbers"; he recognised that the true method of approaching these problems was statistical. If the time was ripe for such experimental work forty years ago, what must we consider it now?