October 20, 1898] 



NATURE 



595 



Prof. Weldon concludes with the observation that " numerical 

 Icnowledge of this kind is the only ultimate test of the theory of 

 natural selection ; or of any other theory of any natural process 

 whatever. " 



It has tested natural selection, and shown that nothing of the 

 nature of a true variety has been established by it. There is no 

 .evolution in the process described at all. 



Does he not speak a little too confidently as to there being no 

 other means of investigation into the procedure of evolution ? 



The true method of establishing this doctrine, as in all other 

 matters of science, I take to be by inductive evidence and ex- 

 perimental verification. By these it has been proved that true 

 varietal changes are produced by what Darwin called " the 

 definite action of changed conditions of life," and he added that 

 when this was the case "a new sub- variety would be produced 

 without the aid of natural selection" ("Animals and Plants 

 •under Domestication," vol. ii. pp. 271, 272). 



In support of this contention of Darwin's I shall be happy to 

 supply Prof. Weldon with an abundance of facts collected in 

 my book, "The Origin of Plant. Structures," if he will promise 

 to read it, entirely unbiassed by his established belief in the 

 efficacy of natural selection. George Henslow. 



80 Holland Park, W. 



The points raised by Mr. Cunningham are numerous, and I 

 trust that he will not think me wanting in courtesy if I make my 

 answer to each of them as short as possible. 



(i) I am glad Mr. Cunningham now believes that the for- 

 tuitous character of animal variation is in many cases indis- 

 putable, so that he no longer holds the view of chance adopted 

 •byEimerand others (^. Eimer, "Organic Evolution," translated 

 by J. T. Cunningham. Macmillan, 1890). 



(2) I cannot agree that the question, which the theory of 

 natural selection attempts to answer, is the question " whether 

 a given modification . . . originated accidentally, or as the 

 Jesuit of a rlefinite ascertainable cause." Without discussing 

 the conception of an "accident" implied in this phase, I fail to 

 see that tlie theory of natural selection involves a theory of the 

 origin of variation \ all it asserts is that the variation which is 

 known to occur does affect the death-rate. 



(3) The well-known fact, that a change in surrounding con- 

 ditions often produces a change in the character of a race by 

 methods other than that of selective destruction, does not dis- 

 prove the co-existence of selective destruction. For example, 

 Mr. Cunningham has not shown that the adaptation of sun- 

 flowers to life in six-inch flower-pots is effected without selective 

 ■destruction ; he has only shown that a portion of the change, 

 associated with life in pots is effected without such destruction. 

 By dividing a sample of seed of known origin into two portions, 

 sowing seeds of one portion in a market garden, seeds of the 

 •other portion singly in a series of flower-pots, Mr. Cunningham 

 has produced two different series of sunflowers, which diff"er in 

 stature and in other characters. I fully accept Mr. Cunning- 

 ham's statement that the plants in the flower-pots were modified 

 without selective destruction. But these plants were not all 

 alike ; and unless it can be shown that each of them produced 

 an equal number of seeds, of equal germinating power, so that 

 if life in flower-pots had been continued each plant, whatever 

 its stature, would have contributed an equal number of equally 

 fertile offspring to the next generation, — unless this can be 

 shown, the action of natural selection is by no means disproved. 

 If among the sunflowers of different stature growing in similar 

 flower-pots, plants of one stature produced more seed than 

 plants of different stature, the plants of that stature were better 

 ■"adapted" to life in flower-pots than the others, and in a 

 struggle to occupy a world filled with six-inch flower-pots, the 

 ■offspring of the more fertile plants would very probably win ; 

 so that a process of natural selection would occur. So far as 

 Mr. Cunningham has described his observations, they do not 

 exclude the possibility that this and other kinds of selection 

 operate. All I am anxious to know, in those cases of organic 

 evolution which I try to understand, is how much of the 

 observed change is due to a process of selective destruction, 

 how much to other causes. 



(4) I heartily agree with the view that it is not possible for 

 selection, under fixed conditions, to modify a species in every 

 direction. It is only possible for natural selection to act so as 

 to produce a race with a minimum death-rate. P'or example, 

 since muddy water of a certain salinity kills broad-fronted crabs 

 more quickly than narrow-fronted crabs, it is probably im- 



NO. 15 I 2, VOL. 58] 



possible for natural selection to increase the frontal breadth of 

 crabs which live in such water. 



(5) In the second part of his letter, Mr. Cunningham attempts 

 an explanation of the evolution observed in Plymouth crabs, 

 which does not involve any selective destruction. For this 

 purpose he makes two hypotheses, one about the growth of 

 crabs, one about the temperature of the sea-shore at Plymouth. 

 Neither of these hypotheses seems to me to fit the facts. It I 

 understand the hypothesis about growth, it is this : that the 

 frontal breadth of a crab depends on its age, while the length of 

 a crab depends not only upon age, but upon temperature and 

 other circumstances affecting it during growth. From this it is 

 deduced that in a group of crabs of the same length, tho.se with 

 narrower fronts are older, those with broader fronts are younger, 

 and 1 suppose that those with equal fronts are assumed to be of 

 the same age. Therefore, when I say that under certain con- 

 ditions the crabs with the broadest fronts die first, Mr. Cun- 

 ningham assumes that under those conditions the youngest 

 crabs die first. I do not know of any published account of the 

 growth of crabs which supports this hypothesis, and the follow- 

 ing facts seem to disprove it : — If we take a group of crabs, of 

 the same length and the same frontal breadth, they are, on this 

 view, nearly of an age : if we keep these crabs till they moult, 

 they will grow at diff"erent rates during the moult ; now those 

 which increase abnormally much in length during the moult, 

 will be younger than average crabs of their new length ; those 

 which show abnormally little increase in length, will be older 

 than the majority of crabs of their new length. Mr. Cun- 

 ningham says that in crabs of a given length, the youngest are 

 the broadest ; therefore those crabs which grew abnormally 

 much ought to have broader fronts than their fellows of their 

 new length, those crabs which grew abnormally little ought to 

 be narrower than their fellows. I have worked out the relation 

 between growth-rate and frontal breadth abnormality in more 

 than 500 cases, and the relation which ought to hold, if Mr. 

 Cunningham's hypothesis were true, does not hold. 



A further disproof of the contention that the youngest crabs 

 died first in my experiments is this : in most of the experiments 

 about equal numbers of crabs of all lengths from 10 to 15 mm. 

 were treated together ; and all crabs used in an experiment 

 were gathered on one day. It will hardly be contended that 

 irregularity of growth goes so far as to produce in the same 

 season crabs between 10 and II mm. long which are of the 

 same age as crabs between 14 and 15 mm long. If the younger 

 crabs died first in my experiments, a mortality of 70 or 80 per 

 cent, might be expected to kill all, or nearly all the shorter 

 crabs, the survivors being derived almost entirely from the 

 longer crabs. This was not the case. For example, in one 

 experiment 200 crabs, lietween 10 and 15 mm. long, were 

 treated with mud until only four were left alive. These four 

 were resjiectively iO'67 mm., 11 '67 mm., 11*43 ran^-* and 

 I2'il mm. long. 



(6) Mr. Cunningham further supposes, and no doubt rightly, 

 that crabs grow faster, within certain limits, the warmer the 

 water in which they are ; so that crabs 10 mm. long, grown in 

 warm water, are probably younger than crabs 10 mm. long 

 grown in colder water. From observations made on the 

 temperature of the Channel water, he thinks it probable that 

 the crabs measured in 1893 were on the whole younger than 

 those measured in 1895, '^"^ those measured this year were 

 oldest of all, — all the crabs being of the same length. The 

 reason tor this is that the water in the Channel was exception- 

 ally hot in 1893, ^"^^ '^o'' some time exceptionally cool this year. 

 But the stony beach where these crabs were collected looks due 

 south, and is uncovered for hours daily, when it is often exposed 

 to the direct rays of the sun. I am most unwilling to believe 

 that the temperature on such a beach was lower during the past 

 summer than in 1893. A further point is that crabs gathered 

 in January ought, if Mr. Cunningham's hypothesis were true, to 

 be distinctly narrower than crabs of the same length gathered in 

 August. Crabs gathered last January were narrower than crabs 

 gathered in August 1893, but they were not narrower than crabs 

 gathered last August. So that all Mr. Cunningham's ingenious 

 hypotheses fail to fit the facts. 



(7) Mr. Cunningham says that there is no evidence of the 

 entrance of fine mud into the gill-chambers of crabs during life. 

 If he will watch a crab breathing in muddy water, or if he will 

 consult the works of Mr. Garstang and other students of the 

 subject, he will see that he is mistaken. I thought the entrance 

 of .such particles into the gill-chamber so well known that I need 



