Nevertheless he proceeds to say that the description of expt. (2), which was repeated eleven times with identical results, was correct "as far as given." That experiment was "from a second series of cultures parallel to the one given, but in which there are other factors involved, which in H. 410 [my (2)] are productive of a typical Mendelian behaviour." He adds he does "not care at this time to make any statement of what these factors are, nor of their relations to the behaviours given in the H. 409, H. 411, H. 409/11 series [my (1), (5) and (3)—(4)] which are the simplest and most easily presented series obtained in the crossing of signaticollis and diversa."
Professor Cockerell's intervention has thus elicited the fact that we have as yet only a small selected part of the evidence before us, even as concerning the effect of temperature on the cross between signaticollis ♀ × diversa ♂. We learn that at the lower temperatures the result was eleven times the expected one, and six times an unexpected one; further, that we owe it to the author's inadvertence that we have come to hear of the expected result at all, and that though he knows the factors which determine the discrepancy, he declines for the present to name them. In these circumstances we can scarcely venture as yet to estimate the significance of these records.
The paper goes on to recount somewhat comparable, but more complex instances in which the descent of the colour of adults and of larvae was affected by temperature in crosses between undecimlineata and signaticollis. As they stand the results are very striking and unexpected, but I think, in view of what has been admitted respecting the former part of the paper, full discussion may be postponed till confirmation is forthcoming.
One feature, however, calls for remark. This second paper is written apparently without any reference to the discoveries related by Tower in his previous book, to which no allusion is made. This is most noticeable in the case of an experiment in which (p. 296, H. 700A) undecimlineata ♀ (the dominant) was mated to signaticollis ♂ with the result that all the offspring were undecimlineata and bred true to that type (Parthenogenesis was tested for, but never found to occur). This experiment was made at a temperature averaging 95° F. ± 3.5° by day and 89° F. ± 4.8° by night, and in a humidity given as 84 per cent. by day and 100 per cent. by night; but in the previous book (p. 294) we are told that pure undecimlineata bred together "under an extreme stimulus of high temperature, 10° C. above the average" and a relative humidity of 40 per cent. gave 11 beetles only, all angustovittata. But reference to the Plate 16, Fig. 2, shows that angustovittata must be exceedingly like signaticollis, having, like it, the elytral stripes obsolete, and if there is any marked difference at all, it can only be in the larvae. It seems strange that if undecimlineata really gives off ova of this recessive type at high temperatures, the fact should not be alluded to in connection with expt. H. 700A, where, as the father was signaticollis, having the same recessive character, their appearance might have been expected not to pass unobserved. The temperature in the older experiment is, of course, not given with the great accuracy used in the second, and it may have been higher still. The humidity also was widely different. Still, in discussing the phenomena we should expect some reference to the very remarkable and closely cognate discovery which Tower himself had previously reported in regard to the same species.[13]
The hesitation which I had come to feel respecting these two publications of Tower's has been, I confess, increased by the appearance of a destructive criticism by Gortner[14] who has examined the parts of Chapter III of Tower's book, in which he discusses at some length the chemistry of the pigments in Leptinotarsa and other animals. As Gortner has shown, this discussion, though offered with every show of confidence, exhibits such elementary ignorance, both of the special subject and of chemistry in general, that it cannot be taken into serious consideration.
Some observations made by Dr. W. T. Macdougal[15] have also been interpreted as showing the actual causation of genetic variation by chemical treatment. Of these perhaps the least open to objection were the experiments with Raimannia odorata, a Patagonian plant closely allied to Oenothera. The ovaries were injected with various substances and from some of the seeds which subsequently formed in them a remarkable new variety was raised. This varying or mutational form was strikingly different from the parental type, with which it was not connected by any intergradational forms, and it bred true. It made no rosette, growing to a much smaller size than the parent, and was totally glabrous instead of being very hairy as the parental type is. I was shown specimens of these plants by the kindness of Dr. Britton in the Bronx Park Botanic Garden in 1907 and can testify to their very remarkable peculiarities. They had a somewhat weakly look, and might at first sight be thought to be a pathological product, but they had bred true for several generations. From the evidence, however, I am by no means satisfied that their original appearance was a consequence of the treatment applied. This treatment was of a most miscellaneous description. Two of the mutants came from an ovary which had been treated with a ten per cent. sugar solution. Ten came from one into which a 0.1 per cent. solution of calcium nitrate had been injected. One was from a capsule which "had been exposed to the action of a radium pencil." Macdougal speaks of these results as decisive, but clearly before such evidence can be admitted even for consideration it must be shown by control experiments that the individual plants which threw the mutant were themselves breeding true in ordinary circumstances. Nothing is more likely than that the mutant was an ordinary recessive. I may add that Mr. R. H. Compton made a number of experiments with Raimannia odorata, raised from seeds kindly given me by Dr. Britton, injecting the ovaries with a variety of substances, including those named by Macdougal; but though a numerous progeny was raised from the ovaries treated, all were normal. Macdougal relates also that some mutational forms came from ovaries of Oenothera Lamarckiana exposed to radium pencils, and also from Oenothera biennis injected with zinc sulphate a peculiar mutant was raised, but taking into account the frequency of these occurrences in those species, he very properly regarded this evidence as of doubtful application. In a later paper,[16] however, he has returned to the subject and affirms his conviction that the appearance of a mutant among seedlings raised from an ovary of Oenothera biennis treated with zinc sulphate was really a consequence of the injection, saying that the variation previously observed in the species was afterwards shown to be due to fungoid disease. The circumstances to which he mainly points in support of his view is that the mutation bred true, but this is only evidence of its genetic distinctness, which may, of course, be admitted by those who remain unconvinced as to the original cause of its appearance. He adds that he is making similar experiments with some twenty genera; but what is more urgently needed is repeated confirmation of the original observation. When it has been shown that this mutation can be produced with any regularity from a plant which does not otherwise produce it on normal self-fertilisation, the enquiry may be profitably extended to other plants.
A curious and novel experiment, which however, led ultimately to a negative result, was made by F. Payne. Many discussions have been held respecting the blindness of cave animals. The phenomenon is one of the well-known difficulties, and most of us would admit that the theory of evolution by the natural selection of small differences does not offer a really satisfying account of it. Those who believe in the causation of such modifications by environmental influences and in their hereditary transmission make, of course, the simple suggestion that the darkness is the cause of the loss of sight, and that disuse has led to the reduction of the visual organs. Payne bred Drosophila ampelophila, the pomace-fly (which is easy to keep in confinement, fed on fermenting bananas), for sixty-nine generations in darkness. At the end of that period there was no perceptible change in the structure of the eyes, or in any other respect. The number of generations may possibly be regarded as insufficient to prove anything, but comparing them, as he does, with the generations of mankind, we see that they correspond with a period of about two thousand years, an interval far longer than those which many writers in particular cases have deemed sufficient.
In his first paper Payne states that, though no structural difference could be perceived, the flies which had been bred in the dark reacted less readily to light than those which had been reared under normal conditions, and he inclined to think that the treatment had thus produced a definite effect. After more careful tests, however, he withdrew this opinion. It proved that both individual flies and individual groups of flies, both of those bred in the light and of those bred in the dark, differed greatly in their reactions, which were measured by counting the time that it took for a fly to travel to the light end of a covered tube, various sources of error being eliminated. He found further that these differences of behaviour were not inherited in any simple way, but he is disposed to attribute them to accidental differences in the nature of the food, an account which seems probable enough.[17]
In several recent publications Blaringhem[18] has described the origin of many abnormal forms of plants, especially of maize, which he attributes to various mutilations practised upon the parents. Respecting these the same difficulty which has been expressed in other cases reappears, that before drawing any conclusion as to the value of such evidence we require to know that the plants treated belong to a really pure line, which if left to nature in the ordinary circumstances of its life in that locality would have had normal offspring. Abnormalities abound in the experience of everyone who examines pans of seedlings of almost any species of plant, and in maize they are well known to be exceptionally common. Some of those which we meet with when we attempt to ripen maize in this country are very similar to those which Blaringhem describes, consisting in irregularities in the distribution of the sexes, in the shapes of the panicles, etc. Many of these are doubtless imperfections of development, due to the dullness of our climate, but others are presumably genetic and would recur in the offspring however treated. If some one working in a climate where maize could be raised in perfection would repeat these experiments, and show that a strain which was thoroughly reliable and normal in its genetic behaviour did, after mutilation, throw the miscellaneous types observed by Blaringhem, that would be evidence at least that the development of the seed could be so influenced by injury to the parental tissues that its properties were changed. Such evidence could be used for what it is worth; but pending an inquiry of this kind I am disposed to regard these observations of variation following on parental injury as suggestive rather than convincing.
Some evidence of a remarkably interesting kind has been collected by J. H. Powers[19] respecting the structure and habits of Amblystoma tigrinum, which led him to the conclusion that striking differences in the form, anatomy, and developmental processes could be effected directly by change in the conditions of life. It is well known that a profusion of forms, distinct in various degrees, is grouped round Amblystoma tigrinum. Some of these are believed to be geographically isolated, others occur together in the same waters, and, as usual, authorities have differed greatly as to the number of names to be given. These forms were studied in detail by Cope who described them in the Batrachia of North America. The view which he inclined to take was that the individual variations of Amblystoma tigrinum resulted from variations in the time and completeness of the metamorphosis, and these were regarded as due to external causes, such as differences in season, temperature, and geographical conditions. Powers, however, states that collecting within a radius of six or eight miles he found almost if not quite the whole "gamut of recorded variation in this species." Some, however, as he states, occurred rarely except under experimental conditions, but considerable differences in temperature were not found necessary in producing them. Every year, he says, he has been able to add to the number of peculiar types found in the same small area in nature, until the amount of natural variation at least equals that seen by Cope in the collections of the National Museum and those of the Philadelphia Academy.