Third International Conference on Genetics (1906) pp. 98-113

DOES HYBRIDISATION INCREASE FLUCTUATING VARIABILITY?
By PROFESSOR W. JOHANNSEN, University of Copenhagen.

THE problem of heredity is the subject of very diligent study at the present time. Two different methods of investigation have been followed by workers, viz. the statistical method and the experimental method, but the results of these two methods do not always seem to agree. And yet in reality agreement must be found.

*The numbers refer to the list of literature at the end of the paper.

Pure statistics in this matter provide a dangerous and uncertain method, not only because the special data are very seldom controllable, but especially because (granting their inherent correctness) a scientific biological analysis of such data cannot be made: it remains quite uncertain whether the numbers in question contain a multitude, or a few, or only one single "sort" of organisms—"biotypes" as I have called them (1).*

In many organisms heredity can only be investigated by the statistical method, as for example in the human race, where experiments are impossible, and in many of the larger animals, such as horses, &c. In all such cases the research is limited to the indications of genealogical tables, stud-books, &c. But such materials are not at all qualified to form a basis for an exact inquiry in heredity. For this purpose data are required which can be controlled, and which are sufficiently specialised to enable them to be separated into different groups from various points of view and in such ways that a true biological analysis may be made in each special case.

The imposing display of mathematical knowledge and refinement with which the "Biometrical School" has dazzled our eyes really proves ineffectual for the true understanding of the physiological laws of heredity, when the mathematical treatment is not based upon an accomplished sorting of the special facts and a biological setting-out of the premises which are to be treated. The most prominent biometrician, Professor Karl Pearson, has in all his work in this biological domain proceeded as if his motto were: "There are no premises; all is treatment!" Indeed this very expression was once flung out against me in a private discussion with a biometrician. Neglect of premises—in a degree quite inconceivable to the experimenting biologists—is the Achilles-heel of biometry, and the whole Biometrical School is therefore standing on very unsafe ground as to the biological value of its results in heredity.

What mistakes and absurdities the neglect of the premises has introduced into the literature of heredity must be known by all who have taken notice of Mr. Bateson's criticisms on "Homotyposis" (2), or—not to go further into polemics—who have seen the recent important little paper by Mr. Hurst (3) concerning the heredity of coat-colour in horses.

Darbishire's (4) change of front with regard to the interpretation of the Mendelian laws shows the awakening of a better understanding as to the value of pure statistics for biology.

It is beyond all doubt that statistical methods have very great importance in many points of research in heredity, but the conditio sine qua non is, as always, a previous competent sifting and arrangement of the data to be used. The questions which interest us in heredity must be formulated biologically, if an answer, biologically applicable, is to be given. But this point has been almost totally neglected by the biometricians.

If anybody makes a study as to the speed of railway-cars, he will of course regard every train or every type of train separately: express trains, local trains, goods trains, and so on. He can then collect details and statistics needful for understanding the traffic as a whole, the train-types, &c. But what would be said of an inquirer who, for solving the problem, collected statistics as to the speed of the different carriage-classes, first, second, and third class, and by this method found out that the average speed of the first-class car was much greater than the average speed of the third-class car—for in the express trains (on the Continent at least) there are only, or almost always only, first and second class cars, while in the local trains the third-class car is in the majority. The result of these statistics would certainly be a truth also, but it would be without any real interest: indeed it would be quite misleading as to matters of railway traffic. I must confess that the main part of biometrical work in questions of heredity somewhat resembles such preposterous statistics.

The mathematical terms in which biometricians have tried to express the "ancestral influence" may in reality be a true result of statistics; but in these statistics the data have mostly not been analysed in a biologically reasonable manner. It is much to be regretted that biometricians, although fairly compelled by the force of argument to see the faults of their premises, still persevere in their "antibiological" proceedings. They seem to confound the statistics serviceable for insurance purposes and also possessing great scientific interest for social questions with the exploration of fundamental laws of biology or physiology.

In the science of biology the rediscovery of Mendel's laws, and the highly important development of Mendelian researches in the last few years, have entirely displaced the general biometrical conception of ancestral influence: it is now evident that in Mendelian cases not the personal qualities of the ancestors but the nature of the zygotes is the essential factor in heredity—and the nature of the zygote is not a more function of ancestral qualities. Statements of averages are here, of course, without value for the experimenting biologist.

The inadequacy of the assumed "ancestral influence" is now granted by all biologists who in their breeding experiments are operating with "traits" which are characterised qualitatively. All the famous Mendelian examples from peas, the results of Correns', Miss Saunders', Techermak's and De Vries's experiments (with plants), Bateson's, Darbishire's, Guaita's, Hurst's, Lang's and others' experiments (with animals) are so plain and clear just because the characters in question are "qualities."

The problem whether the Mendelian segregation is absolutely pure is a matter of a special nature, giving no loophole for the biometrical view of ancestral influence. By impure segregation, when a small quantity of "substance which ought to have been cleaned out" is carried over with the gamete, and finds conditions in the zygote for increasing, impurity may be increasingly augmented. And at last it will become manifest in some individuals in a generation possibly very far removed from the ancestor in question. I have made some experiments on this point, but this is not the place for discussing such matters more closely.

Now I come to the domain in which the stronghold of biometry is situated: the traits which are characterised quantitatively, the types that manifest themselves as differences in degree. Here we meet with the greatest difficulties; here we cannot by simple inspection of any individual decide its type. Here we meet with the "transgressive variability," which makes it quite impossible to judge by inspection whether an individual specimen is a plus-variant of a "little" type or a minus-variant of a "large" type, and so on.

The most important and conspicuous results of the Mendelian experiments relate to traits that do not blend, and with regard to which every simple individual can be grouped in the right class immediately. The results are therefore very striking and well fitted for popular demonstration. In De Vries's celebrated studies of mutations it is almost always such qualities which are regarded; the same may also be said about the extensive and important experiments carried out at Svalöf, in Sweden (5). Here "botanical" characters are almost exclusively regarded, i.e. unmistakable morphological characters, which—as De Vries has said—are " traits not of fluctuating but of mutative nature." These morphological characters are constant except when mutations suddenly give rise to new types. That the pure "pedigrees" of Svalöf in reality have constant types in respect of the quantitatively characterised traits—which give the crops their value—is for me a matter of course, and is also asserted by Professor Hj. Nilsson, of Svalöf. But conclusive scientific researches about all such highly fluctuating characters have not yet been made at Svalöf, where the excellent special workers with good reason have taken "botanical” characters as starting-points for their isolation of types.

The study of heredity as to characters, which by inspection can only be estimated as differences in intensity of the same quality, and which blend in hybridisation, requires special methods. The hybrids with such characters have not yet been examined in a satisfactory manner. In ray experiments with "pure lines" (6) I particularly tried to isolate quantitatively different types from the population in question, and in that way I—as the first, I believe—found out that the Galtonian law of filial regression, declaring that fluctuations are to a certain considerable degree hereditary, is quite wrong and only depends on the presence of several different types in the populations In a population containing only one single type the selection of fluctuations has no action at all! The just-mentioned famous Galtonian law should hereafter—if my view has a general bearing—only be the statistical expression for the circumstance that populations mostly are mixtures, containing different "biotypes." Galton's law is then only a statistical law, but not at all a true biological law. My researches, which have been of no short duration, have given me a very considerable stock of facts in full accordance with this view, thus forming a supplement to the Mendelian and Svalöf experiments as to the appreciation of the effects of selection. And as to my researches we stand upon that ground—quantitative studies—on which the still prevalent conception is based: that selection is able to shift a type in the same direction as that in which the selection of its fluctuations is carried on.

This conception, which I regard as absolutely erroneous, involves the idea that evolution proceeds through continuous variation.

Biological study of the behaviour of the traits that are qualitatively characterised, as in the classical examples of Mendel, does not usually require special mathematical treatment beyond some little calculation of probabilities. But when we attempt researches respecting quantitatively characterised traits, or, it may be, the fluctuations of qualitative traits, we must use the armoury of collective-measuring statistics. Here we find that a long series of prominent mathematicians have worked out methods of computation and other devices. From Gauss and Laplace through Fechner, Quetelet and Galton to Thiele, Lipps, Pearson, Bruns, Kapteyn, Udny Yule, Charlier and Davenport in modern times, the theory of exact observation has been developed and enriched with instructions for the treatment of collective series of measures. As to the finer methods the mathematicians are not at all in accord, and the biologist eager to learn from them is too often a witness to very sharp discussions between mathematicians as to the finer fitting of the mathematical implements which are offered to us. I cannot say that the nature of these discussions gives special reasons to regret that most of the biologists are not able to follow those finer methods in question. And, indeed, even the five or six special equations and formulas for different types of frequency-curves elaborated by Pearson are not of much use for biological students. Here I suppose that Charlier's (7) simplification of the computation, giving only room for two different types of curves, represents a real progress. But also these formulas and equations are too complicated for general biological use; and perhaps future mathematical speculation will give us simpler proceedings.

After having tried to understand the fundamental principles in the publications of Thiele (8) and Charlier, and after studying Davenport's "Statistical Methods" (based especially on Pearson's important work) (9), I suppose that the biologist can satisfy the claim to exactitude without too much trouble in all those cases where the different characters are to be regarded independently. In the case of correlated variability some greater complication is needed. When only one character is to be regarded at a time it is sufficient—and may be said to be necessary—to compute the mean value (average) of the variants, the standard deviation, and, as expressions for the total shape of the frequency curve, two coefficients, the one giving the asymmetry or skewness of the curve, the other giving what Pearson calls the "excess," i.e. indicating whether, and in what manner, the curve surpasses the limits of a binomial curve, skewness not regarded. Of course the total number of observations, n, must also be given. With these five indications the fluctuating variability of a stock as to the traits in question should mostly be sufficiently characterised.

The computation of the mean (average, A) and the standard deviations (s) are well known. The skewness will be determined by the average value of the third powers of deviations from the mean (µ3= (x3f) : n; see Davenport, "Statistical Methods," 2nd edit. p. 116. By complete symmetry µ3=0). As the simplest coefficient of skewness the relation µ3 : σ3  may be regarded; this expression being absolutely independent of any theory of variation. As empirical skewness, therefore, can be indicated S =µ3: σ2. As to the "excess," it must be remembered that the average value of the fourth powers of deviations from the mean (µ4=∑(x4f) : n) shall in case of the normal binomial frequency curve be µ4=3σ4 . Hence µ4 : σ4 =3 indicates that there is no excess. Therefore the formula E=(µ4 : σ4)-3 gives the value and the sign of excess. This value E is, like S, an abstract number and also absolutely independent of any theoretical view of variability.

As to the method of computation, I must refer to the highly practical computation scheme of Charlier, with its excellent controlling system. For the suggestion to limit the computation to the estimation of E and S without following any hypothesis of different types of variation-curves I am indebted to Thiele.

When the biologist in this way is content to use these simple mathematical methods, the legitimacy of which is granted by all authorities, he is able to characterise his series of variation in a manner which gives a very good description of the variability. It is still a desideratum to determine how good the accordance—as to S and E—may be between different series of the same organisms, e.g. the sections of the same pure line in culture in the same garden, &c. The variations in the environments may here give greater disturbances than in respect to the standard deviation. Special researches on this question have been commenced.

As to biological questions concerning heredity and fluctuating variability, it must again and again be emphasised that to procure the facts is the most important but most difficult point in the whole matter. To gather materials from forests, fields and gardens, or—as to man—to send inquiry papers to families, schools and other institutions, may be good for many purposes of social statistics, but it is a quite fallacious method for biological research into heredity questions. And it is a fundamental error to believe that the inspection of variation-curves and correlation-tables can give any certainty to conclusions as to heredity in the true biological or physiological sense of this word. Pearson has, not only in working out his ideas of homotyposis, but perhaps still more by his recent researches (10) in the mental character of school-children, totally omitted to analyse the causes which may be the condition of greater resemblance between brothers and sisters than between children in general. In my own materials of beans I have observed a much greater resemblance between sister-beans than between other beans of the same pure line, and yet all these different individuals (or homotypical organs) have the same value when judged by the offspring's qualities. Here the special resemblance between brothers and sisters has nothing at all to do with heredity as defined by the characters of the zygotes or gametes. I cannot here enter into this matter, but it was necessary to point out this recent biological fault (confusion of social problems with biological—as always by Pearson) because it is important to demonstrate how this very excellent mathematician errs when dealing with biological questions of heredity. Nay, heredity can only be studied in an exact manner by breeding experiments, and here in two ways—analysis and synthesis. The analytical experiment is in its clearest and purest form carried out by working with, "pure lines," i.e. individuals descending from one single homozygotic individual. Pure lines are only to be had in organisms with self-fertilisation (or parthenogenesis); multiplication by graftings, cuttings and other forms of vegetative propagation can here be left out of sight.

"Pure line" is a mere genealogical term; different authors have unfortunately misconceived this meaning, and confounded "pure lines" with "types," "small species," and other such things. I must energetically protest against this misrepresentation of my term "pure line." It indicates nothing more than the warranted purity of descent. By mutation or segregation new types of gametes can be formed within pure lines as well as in genealogical hybrids—the line remains notwithstanding as pure as before in the genealogical sense. Pure lines, therefore, can be monotypical or bi- and polytypical. When we only have quantitatively determined types in view, we may express the fact by the words mono-, bi- and polymodal pure lines. Hitherto, I have only published a few of my researches in monomodal pure lines. As my work is proceeding I hope to publish the results of experiments with bi- and polymodal “lines," the behaviour of which in some points may have resemblance with the segregation in genealogical hybrids. Such occurrences having been found in pure lines seem to me to have a special and peculiar interest affecting also the cytological problems of heredity. The time at my disposal does not allow me to enter into this matter here.

Experiments with monomodal pure lines have shown me that Galton's law of filial regression (in all those cases where this law has been analysed by means of pure lines) is only a consequence of the fact that the populations in question contain different types of organisms. And this composite character of a population cannot be recognised by inspection or any computation of the variations. Selection acts in all such cases apparently as a type-displacing factor; in reality, selection has no altering influence as to the nature of the existing biotypes. Selections act only as sorting factors, more or less perfectly isolating that type or those types which differ most from the average of the population.

The continued researches which I have carried out during the last four years have only confirmed this view, and it will be seen that this is in accordance with the practical experiences from Svalöf. I have tried to find special cases where an effect of selection could be recognised, but in vain. Thus it might be supposed that special selection of the very smallest seeds would give weakly plants, the seeds of which in their turn would be badly nourished, and therefore small; but even this reaction (which must not at all be confounded with heredity) has not been observed with any degree of certainty in my experiments. Small plants gave a less number of seeds—that was all. I hope to be successful in finding such action of selection in pure monomodal lines—in being able to demonstrate the difference between such secondary effect and a veritable type-alteration. It may be that such "spurious" type-alterations are more frequently to be found in breeding experiments with animals. I never heard about them; but they perhaps may have been present in some of De Vries' (11) cases of selection experiments combined with over-nutrition. Unfortunately De Vries' materials have not been homogeneous in my sense of the word.

As to the conception of Galton's (12) law of filial regression, Pearson (13) has the merit of taking in the clearest manner the consequences of that law when he maintains that continued selection is not checked by regression, and must therefore produce an alteration of the type (“Grammar of Science," p. 488). Nevertheless we meet quite erroneous conceptions as to the significance of the above-mentioned Galton's law, so—to take one example only—in the recent book of Lotsy (14), who gives an exposition of these matters without understanding their bearings. It is of course another matter that the often-mentioned law is not a biological law at all, but only the statistical expression of the compound character of the population.

Still more confusion is found as to the celebrated question whether the ambient conditions may be able to produce transmissible alterations in the characters of organisms—i.e. whether exterior conditions may be able to produce an alteration of types. We see here, in place of sober experiments, speculations of a very audacious nature, mostly based upon the confusion of individual adaptative reactions with a supposed alteration of the veritable types (qualities of gametes and zygotes). Most of the 11 "Neo-Lamarckian" literature demonstrates the necessity of exact experiments in all these matters.

It is a pleasure to emphasise the exact experiments of E. Chr. Hansen with yeast-cells (15), cultivated in different ways. Mr. Hansen has operated with "pure lines"; his celebrated studies in fermentations were founded, as is well known, in an exact analysis of yeast-populations—just the same principle that Vilmorin introduced into his heredity experiments more than fifty years ago, the principle which has also been followed in Svalöf and in my own researches.

The influence of the ambient conditions upon the types of organisms can only be studied in reality by means of "pure lines"—If we are to have some warrant as to the meaning of the results: the presumed type-alteration may be nothing but the effect of an unconscious selection in impure, mixed populations. But even in pure lines we have the possibility of mutation, and perhaps extreme conditions may be able to set mutability in action. The whole theory of type-altering by means of altered conditions and direct adaptation is still so vague and floating that it seems unjustifiable to teach it as a sort of semi-scientific creed. As to the evidence from observations in Nature, I cannot omit the striking remarks of Bateson (16), that the differences in ambient nature are gradual, but the differences in organisms from the same locality are specific.

In the domain of hybridology Mendelian analysis has cleared away very much of the obscurity which until recent years was reigning here. It has been the easily appreciable qualitatively characterised traits which here have been the objects of research, and hence in cross-fertilising it has mostly not been necessary to use individuals of which the type. characters in other respects have been determined by special experiments in several generations. Perhaps the neglect of this point may have given to some series of hybrid descendants a greater heterogeneity than would have been encountered by intercrossing individuals belonging to the same pure line of one variety with similarly constituted individuals of another variety (or species).

However it may be in this question; when we proceed to researches in the hybridisation of types that are quantitatively characterised, the highest degree of purity in the two intercrossing varieties or species is required. The material for such hybridisation experiments—to be of scientific value—must be pure lines, the constancy (or, if it may be, the mutability, segregative capacity, and so on) of which has been previously studied in a sufficient number of generations.

We here again touch the fundamental problem as to selection and continuous variability, but now with the complication of intercrossing. Here general scientific opinion sticks to the very popular idea that selection—continued again and again—is able to displace the type of the organisms in question. As to the qualitatively characterised types, Mendelism has shown the inadequacy of selection (17), but as to the quantitatively characterised types the conception is still alive that selection will be able to displace the types in the same direction as the selection is made.

Here I may give some remarks about some criticisms of my paper on heredity in pure. lines (6). Professor Plate (18) has quite misinterpreted my views. I maintain that in (monomodal) pure lines no effect of selection has been proved; I never spoke of an effect which goes back when selection is stopped—here Plate has confounded me with De Vries, who has not worked with pure lines (19). One of the chief points in my little work is that I regard selection of fluctuations as quite ineffective, and hence must emphasise an absolute difference between fluctuation and mutation—at least as to their perceptible manifestations. Here I must see more than "difference of degree." When recently, besides the biometricians and Plate, also an eminent experimenter, Professor Lang (20), basing his views upon very interesting breeding experiments with snails, declares that mutation and fluctuation only are different in degree, then we are at a point of irreconcilable opposition. We are here concerned with one of the most important fundamental problems in heredity—even the very conception of the meaning of "heredity" is affected. This is manifested by such expressions of Lang as "different degrees in the heredity of recurring unaltered characters" ("verschiedene Grade der Erblichkeit unverändert wieder auftauchender Merkmale”), and that heredity may be augmented or diminished in the course of generations (“dass sich die Erblichkeit im Verlaufe der Generationen steigern oder vermindern kann") All these expressions recall Vilmorin's (21) idea as to a greater or smaller hereditary power (“force héréditaire”). But this idea seems to me not only quite superfluous but also wrong, the pretended different degrees of heredity being—in the cases hitherto analysed—the simple consequences of different types existing in the population erroneously regarded as homogeneous, but in reality containing individuals which are fluctuating about a plurality of types.

I anticipate that the results of Lang's researches will eventually prove to be quite reconcilable with my views. As to the experiments which have been fully carried through (with little-fluctuating types) he is a convinced Mendelian. But as to his experiments concerning snail populations with great fluctuations, experiments which are still only in their beginning, Lang seems to have been overpowered by the fluctuations. If the analysis can be carried to an end I cannot doubt that Lang will find distinct types as centres for transgressing fluctuations. The idea of "degrees in heredity" was an advance in Vilmorin's time, but now it only implies that the analysis has not been quite completed. In fact, wherever the essential difference between fluctuation and deviation of type (mutation included) is not conspicuous, we may be sure that a biological analysis has not been performed; it may be that such analysis cannot be effected, or simply that the experimenters have neglected it. At all events I must again say emphatically that results as to which the analysis has not been fully performed, or cannot be effected, must never be used as a basis for fundamental biological theories. We have always to elucidate the unanalysed from the analysed facts; the converse proceeding is wrong.

The most interesting objection against my use of the principle of pure lines is made by Plate. It is that the variability will be diminished when intercrossing is excluded. Lotsy says something similar, if I have understood his somewhat ambiguous remarks. Plate, in his usual clear and sharp manner, expresses his thoughts about my little work. It seems to him that I have proved that self-fertilisation in few generations considerably diminishes the tendency to variation, and that a sort of fixed type is arising in the descent (“dass die Selbstbefruchtung die Neigung zum Variiren nach wenigen Generationen sehr erheblich nachlässt und sich gleichsam ein fester Typus der betreffenden Deszendenten heranbildet”). And Plate says further that the main result of my paper is an indirect proof that intercrossing is a natural means for procuring variations (“"Das wichtigste Resultat, dass freilich in der ganzen Arbeit nirgends erwähnt wird, scheint mir darin zu liegen, dass sie indirekt beweist, dass Wechselbefruchtung ein natürliches Mittel zur Erzeugung von Variationen ist”).

But Plate is here caught by misconceptions and prejudices, which he shares with others; zoologists being very often not familiar with the circumstances of natural self-fertilisation in plants. (The idea that self-fertilisation is something abnormal is very wide-spread; so a prominent anthropologist in a private letter expressed his opinion that my beans in pure lines must soon die out! In nature self-fertilisation may perhaps be more common in plants than cross-fertilisation, and Galton's (22) own experiments stating his law of filial regression were carried out with self-fertilising sweet peas.) In reality there is no trace of indication as to diminution of variability in the course of generations by cultivation in pure lines. There is also no suggestion as to any successive formation of new "fixed" types: the given types have been present from the beginning—they were found and isolated, and the fluctuations about them have not in the least been diminished. How should such marvellous effects of cultivation in pure lines be possible? The self-fertilising plants remain self-fertilisers, whether they are cultivated in numbered places or without numbers. To control this I have made a special research as to the variability in succeeding years—of course there is no alteration, the standard deviation, skewness, and so on, are the same for the same pure line year after year, oscillating to and fro, as all such measures may do.

Hence there is no talk about diminishing variability in pure lines. But should not intercrossing augment variability? We all know that hybridisation gives augmented variability in so far as, by intercrossing of individuals producing different gametes, the different " traits" enter into new combinations, and so on. But this truism is not in question here. Here we have to find out whether intercrossing augments the range of fluctuation or not. Intercrossing of individuals belonging to the same pure line should hardly give any result of interest—and there is no criterion for the success of such an intercrossing experiment, the gametes being of the same nature. But it might a priori be probable—in this respect I can agree with Plate—that intercrossing of individuals belonging to different pure lines would augment the fluctuation in respect of such quantitatively estimated characters which (at least in the first generation of hybrids) blend in hybridisation. Where we have dominant and recessive traits the question is quite different.

For the study of the problem here in question we must first possess well-characterised pure lines, the types and the variability of which have been measured and controlled for several generations. I have chosen four such pure lines for my hybridisation experiments. Three of these pure lines were brown beans (Phaseolus vulgaris, 'Princess beans').

Line E: seeds broad and rather large (petals pure white and yellow).
Line MM: seeds narrow and rather long (petals with trace of purple).
Line BB: seeds broad and small (petals with trace of reddish-purple).
The fourth was black (dark-blue) beans (Phaseolus vulgaris; Belgian haricot vert hâtif).
Line SE: seeds very narrow and long (petals purple).

The dimensions and weight of the beans, being the subjects of the research, will be mentioned more concisely below. Other differences between the four lines will not here be mentioned. The black beans were chosen because the conspicuous difference in colour made it easy to ascertain whether the intercrossing was accomplished or not. A priori it was to be expected that all the hybrids here in question would show the same general behaviour as to the dimensions of the seeds (length, L, breadth, B, and breadth-index, J= 100 B : L). Hence the behaviour of the guaranteed hybrids could be used as a criterion of the hybrid nature of intercrosses between the brown beans.

The hybridisations were performed in the summer 1904 during a visit at Svalöf. My friend Dr. Tedin, the excellent scientific assistant at Svalöf, who is specially trained in the technical difficulties as to intercrossing the leguminous plants, has been so kind as to make all the intercrossings for me. I most heartily thank him for his great amiability on that occasion.

The following hybridisations succeeded:

MM x BB
E x MM
ExSE and SExE.

 A germ produced by intercrossing is developed in a testa belonging to the mother-plants. The germ is "fused" in the "forms" of the motherplants, and here it was quite impossible to recognise in any case whether the hybridisation is realised or not. But when the seeds germinated the hybrids of E x SE were easily recognisable by the purple colour-stripes on the stem—a character belonging to SE. The seeds of these guaranteed hybrids were characterised by dimensions (L, B, and J) the average values of which—each plant regarded separately—were intermediate between the dimensions of the two parent-lines, and the same was found as to the weight of the beans. These characters evidently blend in the hybrid first generation (F1) and are therefore well suited for our studies. It was now a very easy matter to find out the real hybrids of the brown lines, giving also for each plant intermediate values as to the weight and dimensions of seed. Only in one single case I have been in doubt, because the plant in question (of the cross MM x BB) had only two seeds—a number too small for estimating with any certainty.

The question now to be elucidated is whether or not the hybrids have an increased variability as to the weight and dimensions of the beans. The ripe beans were weighed and measured in the same manner as indicated in my paper on "pure lines." Here we shall only regard the results as to the weight, the absolute length and breadth. The correlations between length and breadth are too complicated to be treated here; but in reality the breadth indices of the hybrids are—as we shall see—intermediate between the indices of the relative pure lines.

All hybrid beans have been weighed; but in the crop of 1905 I have weighed some portions taken at random from the pure lines. The results are tabulated in Table I., in which the hybrids are placed between their parent lines.

All indications relate to the crop of 1905.

The heading letters in Table I. signify:—

n the number of individuals.
A the average weight in centigrammes.
σ the standard deviation in centigrammes.
V the coefficient of variability (100 s : A).
S the coefficient of skewness (see p. 102).
E the coefficient of excess (see p. 102).

TABLE I.—WEIGHTS OF BEANS FROM FOUR "PURE LINES" AND THREE OF THEIR HYBRIDS (1905).

  n A σ V S E
Pure line SE (black) 414 36.9 6.47 17.5 - 0.28 - 0.22
Hybrids 902 46,6 7.34 15.7 - 0.38 + 0.24
Pure line E (brown) 446 59.7 6.25 10.5 - 0.19 + 0.69
Hybrids 421 54.8 7.14 13.0 - 0.21 - 0.11
Pure line MM (brown) 722 50.6 6.08 12.0 - 0.32 + 0.61
Hybrids 375 45.3 5.97 13.2 - 0.31 + 0.07
Pure line BB (brown) 612 42.1 6.17 14.7 - 0.72 + 0.84

These numbers do not demonstrate any considerable difference between the variation of hybrids and pure lines. The hybrids have in most of the cases intermediate values between the values of their parent lines, but as to the "excess" the pure lines evidently have much larger deviation from the "normal" curve than the hybrids. It is to be seen in all cases; and with exception of line SE, deviating negatively, the pure lines have a much higher excess than the hybrids.

The same is to be seen in the variation of the dimensions. These are presented in the two following tables, giving respectively the measures of length and of breadth. Here all individuals of the pure lines have been measured; the characteristics of the pure lines are therefore very true. In Table II. A and are expressed in millimetres, the rest of the heading letters have the same significance as in Table I.

TABLE II.—THE LENGTH OF BEANS FROM FOUR "PURE UNES" AND THREE OF THEIR HYBRIDS, (1905).

  n A σ V S E
Pure line SE (black) 414 14.53 0.92 6.4 - 0.62 + 0.66
Hybrids 902 13.92 0.67 6.2 - 0.49 + 0.96
Pure line E (brown) 6004 12.63 0.61 4.8 - 0.59 + 2.84
Hybrids 421 13.53 0.68 5.0 0.00 + 0.02
Pure line MM (brown) 5546 14.01 0.70 50 - 0.79 + 3.08
Hybrids 375 12.76 0.67 5.2 - 0.72 + 1.35
Pure line BB (brown) 6663 11.25 0.63 4.7 - 0.68 + 4.01

In Table III., giving the measures of breadth, A and are also expressed in millimetres. In the column headed J the relative breadths are indicated, i.e. average breadth indices, J=100 breadth length.

TABLE III.—THE BREADTH OF BEANS FROM FOUR "PURE LINES" AND THREE OF THEIR HYBRIDS (1905).

  n A σ V S E J
Pure line SE (black) 414 698 0.36 5.2 - 0.57 + 0.45 47.7
Hybrids 902 7.81 0.42 5.4 - 0.35 + 0.13 56.1
Pure line E (brown) 6004 9.01 0.71 4.6 - 0.60 + 1.33 71.3
Hybrids 421 6.39 0.40 4.7 - 0.12 - 0.42 62.0
Pure line MM (brown) 5546 7.72 0.31 4.1 - 0.45 + 1.07 55.1
Hybrids 375 7.86 0.34 4.3 - 0.25 + 0.11 61.6
Pure line BB (brown) 6663 7.97 0.41 5.2 - 0.61 + 1.01 70.7

As to the dimensions also we cannot find any greater variability in hybrids. But they have always shown a much smaller coefficient of excess than the pure lines. The standard deviation or coefficient of variability being almost identical, this means clearly that the greatest deviations from the mean are relatively more numerous in our pure lines than in their hybrids. These fluctuate more in accordance with the "normal frequency curve" than their pure parent lines. These also have a greater skewness in their curves than the hybrids.

Resuming these experiments, it may be said that the fluctuations as to weight and dimensions in the pure lines were not less than in their hybrids; here was no increased amplitude of variability, offering any better material for selection. The contrary was rather the case as expressed by the higher "excesses" in the pure lines. These results may also be regarded as an answer to the criticism which maintained that my pure lines should present diminished fluctuations!

It is now my task to observe the progeny of the hybrids through a series of generations in the same manner as I have observed several pure lines. To judge from some few breeding experiments in the greenhouse, there will be found Mendelian segregations as to dimensions and weights. This matter will be observed more closely, and the isolation of the new type-combinations shall be carried out. In this manner what may be called "unit-characters" as to length, breadth, indices, weight and so on will be elucidated. I hope to find some quantitatively estimated traits that not only blend in the first generation of hybrids, but do not segregate at all. The exact quantitative study of such hybrids is still to be performed.

At all events it seems to me now that we have no reason to suppose that an augmented fluctuation will be found in the new types which here may be formed by segregations and new combinations. Further research will, I have every conviction, give greater clearness as to the fundamental distinction of true type differences and fluctuations. The way out of the confusion in the struggling theories of heredity and evolution is by exact biological analysis; mathematics may here be a good and indispensable servant, but not the commander! "Treatment "—mathematical, philosophical, and fantastical—may be disputable; what we want —in much higher degree than commonly admitted—are well analysed pure and clear elementary premises.

Continuity of evolution is the most beautiful idea of modern biological philosophy; we all may love this idea and have some hope of its being true, but in reality not one indisputable fact as yet proves it. And are not the results of modern chemistry speaking loudly of discontinuity as a fundamental fact in nature?

APPENDIX.

After writing this paper, I received, by the kindness of Mr. Darbishire, his very interesting pamphlet "On the Differences between Physiological and Statistical Laws of Heredity" (from Memoirs and Proceedings of the Manchester Lit. and Phil. Soc., vol. 1. Part III., 1906). The author attacks his problem on another ground than that upon which my criticisms as to statistical treatment of heredity are based; so far we supplement each other. It will be evident to an intelligent reader, that one of the tendencies of my present paper is to emphasise the fact that the biometrician's methods of measuring the "intensity of heredity" are fallacious not only when applied in "predicable cases" (Darbishire p. 37), but also—from a biological point of view—when applied in "non-predicable cases." These comprise all the non-analysed cases (including what may be non-analysable), concerning especially the quantitatively characterised highly fluctuating traits. Here biometry has given us stones for bread, e.g. as to the understanding of the action of selection, as to the problem of discontinuous or continuous evolution, and so on. I am quite in accordance with Mr. Darbishire when he says that "the true function of the biometrician is to give us statistics of average conduct where we cannot predict individual conduct." And this may perhaps suffice for many important problems of sociology (with pleasure I will say "biological sociology" if desired), but it has no value at all for the biology of heredity and evolution, the aim of which is to elucidate the origin and conduct of the veritable types of organisms, the "biotypes." Here biology must try to make the "non-predicable" predicable, by a sound analysis avoiding statistics of heterogeneous impure masses. The biometrical "truths" as to such masses may be able to confuse the views of biologists just so much as Weismann's speculations on the "All-sufficiency of Natural Selection"—both operating with false premises: impure masses regarded as homogeneous aggregations.

SOME REFERENCES TO LITERATURE.

  1. JOHANNSEN.—Arvelighedslaerens Elementer. (Kobenhavn, 1905.) (Translation in preparation.)
  2. BATESON.—Variation and Differentiation. (Printed for the Author, Cambridge University Press, 1903.)
  3. HURST.—On the Inheritance of Coat Colour in Horses. (Proceedings of the Royal Society, B, vol. 77, p. 888, 1906.)
  4. DARBISHIRE.—On the Supposed Antagonism of Mendelian to Biometrical Theories of Heredity. (Memoirs and Proceedings of the Manchester Lit. & Phil. Soc., vol. 49, Part II., Nr. 6, 1905.)
  5. DE VRIES.—Die Svalöfer Methods zur Veredelung, &c. (Archiv für Rassen- und Gesellschafts-Biologie 8 Jahrg., p. 825, 1906.)
  6. JOHANNSEN.—Ueber Erblichkeit in Populationen und in reinen Linien. (Jena, Fischer, 1903.)
  7. CHARLIER.—Researches into the Theory of Probability. (Lunds Universitets Xrsskrift, N.F. AM. 2, Rd. 1, Nr. 5, 1906.)
  8. THIELE.—Theory of Observations (London, 1903); and Forelaesninger over Almindelig Iagttagelseslaere. (Kobenhavn, 1889.)
  9. DAVENPORT.—Statistical Methods, with Special Reference to Biological Variation. (2nd Edit., New York, 1904.)
  10. PEARSON.—On the Laws of Inheritance in Man. II. (Biometrika vol. 8, p. 131, if. 1904.)
  11. DE VRIES.—Alimentation et Selection. (Vol. jubil. Soc. biol. de Paris, 1899.)
  12. GALTON.—Natural Inheritance. (London, 1889.)
  13. PEARSON.—The Grammar of Science. (2nd Edit., 1900.)
  14. LOTSY.—Vorlesungen über Descendenztheorien. I. (Jena, Fischer, 1906.)
  15. E. CHR. HANSEN.—Om Variationen hoe Saccharomyceterne. (Meddelelser fra Carlsberg Laboratoriet V., 1900, p. 1.)
  16. BATESON.—Materials for the Study of Variation. (London, 1894.)
  17. It is here sufficient to refer to Bateson, Presidential Address to Section D, British Association's Report, Cambridge, 1904, p. 574.
  18. PLATE.—Review of my "Erblichkeit in Populationen," &c. in Archiv für Rassen- und Gesellechafts-Biologie, I., p. 187, 1904. See also Plate's article "Die Mutationstheorie im Lichte zoologischer Tatsachen." (Comptes rendus du 6me Congrès intern, de Zoologie, 1904-1905.)
  19. MACDOUGAL (AND VAIL, SHULL, AND SMALL).—Mutants and Hybrids of the OEnotheras (Papers of Station for Experimental Evolution at Cold Spring Harbour, New York, Nr. 2 Washington, 1905), emphasises and exemplifies the necessity of analysing the species before entering on the question of mutation. This is quite in accordance with my own views.
  20. LANG.—Ueber die Mendel'schen Gesetze, Art- und Varietatenbildung, Mutation und Variation, insbesondere bei unseren Hain- und Gartenschnecken. (“Verhandl. d. Schweiz. Naturforschenden Gesellschaft, Luzern, 1905," 1906.)
  21. VILMORIN.—Notices sur l'amélioration des plantes par le semis. (Nouvelle édition, Paris, 1886.) Contains Louis Vilmorin's highly interesting papers on heredity from the time before Darwin.
  22. GALTON.—Natural Inheritance. (London, 1889.)

DISCUSSION.

The President: Professor Johannsen has been dealing with a problem of extreme difficulty. He analyses types according to their quantitative relations, and he shows that what we call one type is in reality a great number of types which are each true to a certain definite average weight. His experiments go to indicate that these averages are in themselves pure factors. What happens when these pure types differentiated by small fluctuations are crossed, we do not know, but there is a suggestion that segregation occurs.

Professor Plate, of Berlin: If you take a pure type which is always self-fertilised, you cannot expect variation; but as soon as you change the outward conditions of the pure type—I do not say that the variations would not be small, but on the one side or the other there will be continuous variation. If the continued conditions are fixed, there would not be any change, either to the one side or the other, and that would be what Darwin calls "continuous variation." Therefore Professor Johannsen has not convinced me that continuous variation does not exist. If we look into nature we can always get continuous variation. For instance, I have studied snails which are to be found in the Bahama Islands, and although there were the greatest variations they were continuous.

Mr. G. U. Yule, University College, London; I am afraid I have not yet been won entirely to Professor Johannsen's views. It is quite true that he has not been able to observe any differentiation, even though he has selected the weight or width of his beans throughout five generations; but, as I suggested in a short review of Professor Johannsen's work, it would be quite possible that that should happen if the variations due to environment were large compared with the variations in the germinal types, and I think it will be found that the somatic variation in these beans is very large indeed compared with the germinal variation. If, under such circumstances, you select according to somatic character, there will be only a very slight selection of germinal types, and this may well be masked by somatic fluctuations. I judge, from other things we know, that the germinal variation cannot be absolutely zero. To justify this statement I fear I must mention a quantity which I shall have to mention again later on, and that is the correlation-coefficient of the biometrical school. We know few such correlation coefficients for cases of self-fertilisation or vegetative reproduction, but the coefficients that have been determined exhibit one common characteristic—the coefficients of the offspring with the higher ancestry are always less than the correlation with the parent. If Professor Johannsen's view, as I understand it, were true, and the germinal type were absolutely and rigidly fixed, then in the mass of the population, the correlation between the offspring and the grandparent would be identical with that between the offspring and the parent. We have not many data, as I have said, but such as exist seem against Professor Johannsen's view, and accordingly I feel inclined to hold my judgment in suspense until the question has been further studied.

The President: We must expect the answer to come from later generations. Pending further tests we are bound to suspend our judgment.

Mr. C. C. Hurst, Hinckley, England: In view of the discussion I might remark that I have also been carrying out some experiments of the same nature as those Professor Johannsen has been engaged upon. I have chosen the Dutch rabbit, which is very fluctuating, and I might say that up to now the results are of a purely negative nature. I hope to be able to report shortly, but at present the continuous variations are hereditable. Professor Johannsen also stated that Mendel's experiments did not touch the question of continuous variation. That is true in a sense; but I should like to point out that before Mendel's experiments were begun, our general ideas of variation were that continuity was the rule and discontinuity almost the exception. I think the solitary person who recognised the great value of discontinuity was our worthy President, Mr. Bateson, long before Mendel was known, and when the rest of us were sticking to Darwin's continuity. When we made an experiment with sweet peas, before Mendel was known, and we found in the F2 generation purples, reds, and whites, and all the different gradations of colour, we should at first sight have said that that was the effect of variation. Now we know, from the experiments of Bateson and Miss Saunders, that discontinuity is the rule with sweet peas. Therefore I think it is only fair to point out that the supposed continuous variations are really discontinuous. We shall find that almost all the hereditable characters are discontinuous in nature, and that the continuous variation is merely somatic and altogether apart from heredity.