CHAPTER II

EXAMPLES OF EXPERIMENTAL PHYSIOLOGICAL CRITICISM

EXPERIMENTAL criticism rests on absolute principles which must guide experimenters in noting and interpreting the phenomena of nature. It will be particularly useful in the biological sciences where prevailing theories are so often propped up with false ideas or based on poorly observed facts. We shall here deal with examples recalling the principles, by virtue of which we may well judge physiological theories, and discuss the facts on which they are based. As we already know, our criterion par excellence is the principle of experimental determinism united with philosophic doubt. In this connection, let me again recall the fact that, in science, we must never confuse principles with theories. Principles are scientific axioms; as absolute truths, they are an immutable criterion. Theories are scientific generalizations or scientific ideas which sum up our present state of knowledge; they are always relative truths, destined to change with the progress of science. So if we posit as a basic conclusion, that we must not believe absolutely in the formulæ of science, we must, on the contrary, believe absolutely in its principles. Men who too completely believe in theories and neglect principles, take the shadow for reality; they lack any solid criterion and are liable to all the consequent sources of error. In every science, progress consists in so changing our theories as to get more and more perfect ones. Indeed, of what use would study be, if we could not change our opinions or theories? But principles and the scientific method are higher than theory; they are immutable and can never change.

Experimental criticism must therefore forearm itself, not only against belief in theories, but against being led astray by too highly valuing the words which we have created to picture to ourselves the supposed forces of nature. In every science, but in the physiological sciences more than all others, we are in danger of deceiving ourselves about words. We must never forget that our characterizations of the

phenomena of nature, as mineral or vital forces, are merely figurative language by which we must not allow ourselves to be duped. The only realities are manifestations of phenomena and the conditions of these manifestations which remain to be determined; experimental criticism should never lose sight of that. In a word, experimental criticism casts doubt on everything except the principle of scientific, rational determinism in the realm of facts (pp. 52-67). It is always founded on this same base, whether we direct it against ourselves or others; that is why we shall usually present two examples in what follows, one chosen from our own researches, the other from other men's work. In science, indeed, we must not only try to criticise others, but every man of science must always be a severe critic of himself. Whenever he proffers an opinion or proposes a theory, he must be the first to try to control it by criticism and to base it on well observed and accurately determined facts.

I. THE PRINCIPLE OF EXPERIMENTAL DETERMINISM DOES NOT ADMIT OF CONTRADICTORY FACTS

First example.-It is now a long time since I announced an experiment which greatly surprised physiologists: the experiment consists in making an animal artificially diabetic by means of a puncture in the floor of the fourth ventricle. I was led to try this puncture as a result of theoretical considerations which I need not recall; all that we here need to know is that I succeeded at the first attempt, i.e., that I saw the first rabbit on which I operated become strikingly diabetic. But I afterward had the experience of repeating the experiment many times (eight or ten times) without getting the same result. I then found myself in presence of a positive fact and of eight or ten negative facts; yet I never thought of denying my first positive experiment in favor of the negative experiments which followed it. Thoroughly convinced that my failures were due only to not knowing the true conditions of my first experiment, I persisted in experimenting, to try to discover them. As a result, I succeeded in defining the exact place for the puncture, and showing the conditions in which the animal to be operated on should be placed; so that we can to-day reproduce artificial diabetes whenever we place ourselves in the conditions known to be necessary to its appearance.

Let me add to the above a reflection showing how many sources of error may surround physiologists in the investigation of vital phe nomena. Let me assume that, instead of succeeding at once in making a rabbit diabetic, all the negative facts had first appeared; it is clear that, after failing two or three times, I should have concluded, not only that the theory guiding me was false, but that puncture of the fourth ventricle did not produce diabetes. Yet I should have been wrong. How often men must have been and still must be wrong in this way! It even seems impossible absolutely to avoid this kind of mistake. We wish to draw from this experiment another general conclusion which will be corroborated by subsequent examples, to wit, that negative facts when considered alone, never teach us anything.

Second example. Every day we see discussions which remain profitless for science, because we are not thoroughly enough imbued with the principle that, since every fact has its own appropriate cause, a negative fact proves nothing and can never destroy a positive fact. To prove what I am setting forth, I will quote the criticisms which M. Longet formerly made on Magendie's experiments. I choose this example, on the one hand, because it is highly instructive, and, on the other, because I was involved in it, and know all the circumstances accurately. Let me begin with M. Longet's criticisms about Magendie's experiments on the properties of recurrent sensitivity in the anterior spinal roots. The first objection which M. Longet makes to Magendie is that he changed his opinion as to the sensitivity of the anterior roots, holding in 1822 that the anterior roots were scarcely sensitive, and in 1839 that they were very sensitive, etc. Thereupon M. Longet exclaims: "Truth is single; from the midst of these contrasted, contradictory assertions of the same author, let the reader choose if he dare." (loc. cit., p. 22.) Finally M. Longet goes on, "M. Magendie ought at least to have told us,-to get us out of our difficulties,-which of his experiments were properly made, the 1822 experiments or those in 1839." (loc. cit., p. 23.)

1

These criticisms are all ill founded and completely violate the

F. A. Longet, Recherches oliniques et expérimentales sur les fonctions des faisceaux de la moelle épinière et des racines des nerfs rachidiens, précédées d'un Examen historique et critique des expériences faites sur ces organes depuis Sir Ch. Bell, et suivies d'autres recherches sur diverses parties du système nerveux Archives générales de médecine, 1841, 3d Series, Vol. X, p. 296 and Vol. XI p. 129).

rules of experimental scientific criticism. In fact, if Magendie in 1822 said that the anterior roots were insensitive, and if he said later in 1839 that the anterior roots are very sensitive, it was because he then found them very sensitive. We do not have to choose between the two results, as M. Longet believes; we must accept them both and merely explain and define them in their respective conditions. When M. Longet exclaims: "Truth is single," does he mean that if one of these results is true, the other must be false? By no means; they are both true, unless we say that in one case Magendie lied, and that is certainly not the critic's idea. But by virtue of the scientific principle of the determinism of phenomena, we must absolutely affirm a priori that in 1822 and in 1839 Magendie did not see the phenomena in identical conditions; the differences in conditions are precisely what we must seek out and define, so as to harmonize the two results and thus find the cause of variation in the phenomenon. The only objection which M. Longet might have made to Magendie was that he did not himself seek out the reason for the difference in the two results; but the criticism by exclusion that M. Longet directed against Magendie's experiments is false and, as we said, out of harmony with the principles of experimental criticism.

We cannot doubt that the above criticism is sincere and purely scientific; for in other circumstances connected with the same discussion M. Longet directed against himself the same criticism by exclusion and in his own criticism was led into the same kind of mistake as in the criticism directed against Magendie.

In 1839 M. Longet, like myself, was working in the laboratory of the Collège de France when Magendie discovered the sensitivity of the anterior spinal roots and showed that it is derived from the posterior roots and returns by the periphery, whence the name reverse sensitivity or recurrent sensitivity which he gave it. Like Magendie and me, M. Longet then saw that the anterior root was sensitive and that it was so under the influence of the posterior root, and he saw it so clearly that he claimed discovery of the latter fact for himself. But later, in 1841, when Longet wished to repeat Magendie's experiment, he found no sensitiveness in the anterior root. In rather amusing circumstances, M. Longet thus found him

* Longet, Comptes rendus de l'Académie des sciences, Vol. VIII, p. 787, June 3 and 10; Comptes rendus de l'Académie des sciences, June 4; Gazette des hôpitaux, June 13 and 18, 1839.

self in exactly the same position in relation to the same fact of sensitiveness in the anterior spinal roots with which he had reproached Magendie, i.e., M. Longet in 1889 saw that the anterior spinal root was sensitive and, in 1841, saw that it was insensitive. Magendie's sceptical mind was not disturbed by these seeming obscurities and contradictions; he went on experimenting and always said what he saw. M. Longet's mind, on the contrary, wished to have the truth on one side or the other; that is why he decided in favor of the 1841 experiments, i.e., the negative experiments; and here is what he said: "Though at that time (1839) I brought forward my claim to the discovery of one of these facts (recurrent sensitiveness), now that I have made many and varied experiments on this point in physiology, I combat these very facts as erroneous, whether they are regarded as Magendie's property or my own. When we have made a mistake, the service which we owe to truth requires that we should never fear retraction. I shall here only recall the insensitivity of the anterior roots and sheaves which we have so often proved, so that the reader may readily understand how meaningless are these results which, like so many others, merely encumber science and embarrass its advance." After this confession, we may be sure that M. Longet is animated only by a desire to find the truth, which he proves when he says that we must never be afraid of retraction if we have made an error. I wholly share this feeling. Let me add that it is always instructive to acknowledge an error. The precept, therefore, is excellent, for we are all likely to make mistakes, except those of us who do nothing. But the first requirement in acknowledging a mistake is to prove that there is an error. It is not enough to say: I was mistaken; we must say how we were mistaken; the important point is precisely that. Now M. Longet explains nothing; he seems purely and simply to say: In 1839 I saw sensitive roots; in 1841, I saw insensitive ones more often, therefore I was mistaken in 1839. Such reasoning is inadmissible. Here, in fact, are a number of experiments in 1839, à propos to the sensitivity of anterior roots,-experiments in which the spinal roots were cut one by one; and to note their properties, their ends were pinched. Magendie wrote half a volume on the subject. Later when people fail to obtain the same results, the question cannot be decided simply by saying that we made a mistake the first time and are right the second time. After all, why 'Longet, loc. cit. p. 21.