Problems of Genetics

by William Bateson

The elaborate experiments of Schröder with Abraxas grossulariata are difficult to follow and are complicated by the fact that the series which was submitted to abnormal temperatures was derived from an abnormal original pair. From the evidence given it is not clear to me whether the temperature had a distinct effect. This insect, like Arctia caja, produces an immense number of variations (especially in the amount of the black pigment) and as most of these are, I believe, reared in domestication for sale, it is highly probable that the species is easily influenced by cultural conditions.

Schröder describes two other experiments which have been accepted by Semon and other supporters of the view that acquired characters are transmitted. In the first, Phratora vitellinae, a phytophagous beetle living on the undersides of leaves, was used. It naturally feeds on Salix fragilis, a species without a felt, or tomentum, on the underside of the leaves. Larvae were transferred to another willow (near S. viminalis) which has the undersides of the leaves felted. The larvae took readily to the new food, pushing the tomentum before them as they gnawed the leaves. They came to maturity and when they were about to lay their eggs they were given a free choice between S. fragilis and the tomentose species. The greater number of ovipositions, 219, took place on fragilis, and there were 127 on the tomentose bush, which we are told was six times as large as the fragilis. The larvae from fragilis were next put on the tomentose species and reared on it. When they became imagines they were similarly given their choice, with the result that there were 104 ovipositions on the tomentose species and only 83 on fragilis. In the next generations there were 48 ovipositions on the tomentose and 11 on fragilis. Finally the fourth generation made 15 ovipositions on the tomentose and none on fragilis.

The difficulty about such experiments is obviously that one has no assurance that the change of instinct, in so far as there is any, may not be a mere consequence of the captivity. It must, besides, be extremely difficult to arrange the experiment so that there is really an equal choice between the two bushes, when one stands beside the other. Przibram, in quoting this case, considers that as the tomentose bush was about six times as large as the fragilis, some indication of the relative attractiveness of the two may be obtained by dividing the ovipositions on the larger bush by six, but I imagine the matter must be much more complex.

Schröder's second example is not more convincing, in my opinion, though Semon regards it as one of the most important pieces of evidence. It concerns a leaf-rolling moth, Gracilaria stigmatella, the larva of which is said normally to make its house by bending over the tips of the sallow leaves on which it feeds. Schröder placed larvae on leaves from which the tips had been cut, and these larvae made their houses by rolling over the sides of the leaves. Their offspring were again fed on leaves without tips, and as before, they rolled in the leaf-margins either on one side or both. The offspring of this second generation were then fed on entire leaves. There were 19 houses made by these (?19) larvae, and of them 15 were normal, made by folding down the tips of the leaves, while 4 were abnormal, made by rolling in the leaf-margins. Schröder says that in nature he has only twice seen abnormal houses; but it is clearly essential not only that the frequency of such variability in nature should be thoroughly examined, but also that we should know whether when the species is bred in captivity these irregularities of behaviour do or do not occur when the larvae are fed on uninjured leaves.

The famous case of Schübeler's wheat is revived by Semon. The story will be familiar to most readers of the literature of the subject. Briefly it is that annuals, especially wheat and maize, raised from seed in Central Europe take more time in coming to maturity and ripening than similar plants raised in Norway, where the summer days are much longer. The received account is that he imported seed especially of maize and of wheat from Central Europe to Norway and found that in successive years the period of growth and ripening was increasingly reduced. After two generations seed of the accelerated wheat was sent back to Breslau where it was grown, and was found to ripen rather more slowly than in Norway, but much more quickly than the original stock had done. The facts recorded by Schübeler[6] are that he received seed from Eldena, which is on the Baltic near Greifswald. The variety is described as "100 tägiger Sommer Weizen," but no more exact record of its behaviour in Germany is given. This wheat, grown at Christiania in 1857, took 103 days to harvest. Its seed was again grown in Christiania in 1858, and took 93 days, and sown again in 1859 it took only 75 days, 28 days less than in the first year of cultivation in Norway. Seed of the 1858 crop was sent to Breslau, and grown there by Roedelius in 1859; it took 80 days. Evidently before such a record can be used as proving an inheritance of acquired characters numbers of particulars should be forthcoming. The view that Johannsen has taken is that the result was probably due to unconscious selection of the earlier individuals among a population consisting of many types of various compositions. Some effect may no doubt be ascribed to that cause, but I cannot think that alone it would account for the results. My impression is rather that they were produced by differences in the cultivation and especially in the seasons. Research of an elaborate character would be necessary in order to eliminate the various sources of error, and nothing of the kind has been done; nor does Semon allude to these difficulties in prominently adducing Schübeler's evidence. A difference of even three weeks in time of harvesting may easily be due to variation in the season. It would in any case be difficult to analyse the meteorological conditions, and to decide how much effect in postponing or accelerating the harvest might be due to cold days, to cloudy days, to wet weather, to fluctuations in average temperature, to hot days, and other such incidents occurring at the different periods of growth, even if they were specially watched while the experiments were in progress, and at this distance of time such analysis is practically impossible. Without careful simultaneous control-experiments this evidence is almost worthless. The director of the Meteorological Office[7] has, however, kindly sent me some details of the weather at Breslau from 1857 to 1860, and I notice that as a matter of fact July, 1859, was an exceptionally hot month, having an average of 2.67° C. above the mean for the twenty years 1848-1867. June in that year was slightly (0.31° C.) below the mean and May slightly above it (0.18° C.). August was also abnormally hot, 2.35° C. above the average. The Breslau wheat was sown on May 19 and harvested on August 6. There was a cold spell from May 11 to 14, which this wheat escaped, as it was sown on May 19. In the other years the cold spell came much later. These elements of the weather may possibly have done something to hurry the ripening in 1859. It unfortunate that we are not told how long similar wheat from Breslau seed took to ripen in that year.

As regards the Norway cultivations we have the average monthly temperatures recorded by Schübeler, though he does not discuss them in connection with this special problem. It is quite clear that 1857, in which the period was 103 days, was an exceptionally cold summer, especially as regards the months of June and July, but though there was, so far as the temperature records go, no great difference between 1858 and 1859, the year 1859, in which the period of ripening was the shortest, was somewhat colder in Norway than 1858. But we have the further difficulty that there were ten days difference in sowing, for in 1858 the sowing was made on May 14, and in 1859 on May 24. With all these possibilities uncontrolled, and indeed unconsidered, I am surprised that Semon should claim these experiments as one of the chief supports for his views.

Schübeler's other allegations respecting the influence of climate on plants grown in various places and especially at different elevations in Norway have been destructively criticised by Wille[8] to whose paper readers interested in the subject should refer.

Before the appearance of Wille's criticisms Wettstein[9] made a favourable reference to Schübeler's work, accepting his conclusion. He states also that he has himself made analogous experiments with flax, finding that the length of the period of development and a series of morphological characters show an adaptation to local conditions, and that on transference of seed to other conditions the previous effects are maintained. No details, however, are given, and I do not know if anything more on the subject has appeared since. The other examples cited by Wettstein, such as the observations of Cieslar on forest-trees and those of Jakowatz on gentians seem to me open to all the usual objections applicable to evidence of this kind. Such work, to be of any value for the purpose to which it is applied, must be preceded by a study of the normal heredity and of the variations of the species.

Most of the recent writers (Semon, Przibram, etc.) on the inheritance of acquired characters accept the story of Brown-Séquard's guinea pigs, which are said to have inherited a liability to peculiar epileptiform attacks induced in their parents by various nervous lesions.

The question has been often debated and several observers have repeated the experiments with varying results, some failing to confirm Brown-Séquard, others finding evidence which in various degrees supported his conclusions. Recently a new and especially valuable paper has been published by Mr. T. Graham Brown[10] which goes far towards settling this outstanding question. He states that "the Brown-Séquard phenomenon is nothing more or less than a specific instance of the scratch-reflex," and it is due to a raised excitability of the mechanism of this reflex. This raised excitability is the character acquired as a consequence, for instance, of the removal of part of one great sciatic nerve. The nature of this raised excitability and its causation are discussed and elucidated, but this part of the work is not essential to the present consideration. Mr. Graham Brown in his summary of conclusions remarks that it is very difficult to see how this condition of raised excitability can be transmitted to the offspring, and this comment which might be made in reference to any of the alleged cases certainly applies with special cogency to the present example.