An Introduction to the Study of Experimental Medicine

Once in possession of the first discovery that sugar is formed in animals after death as during life, I wished to carry my study of this singular phenomenon further; I was then led to find that sugar is produced in the liver with the help of an enzyme reacting on an amylaceous substance which I isolated and which I called glycogenous matter, so that I succeeded in proving in the most clear-cut way that sugar is formed in animals by a mechanism in every respect like the mechanism found in vegetables.

This second series of facts embodied results, which are also firmly acquired for science, and which have greatly advanced our knowledge of glycogenosis in animals. I have just very briefly told how these facts were discovered, and how they started with an experimental circumstance that was apparently inconsequential. I quote this case so as to prove that we must never neglect anything in experimental research, for every accident has a necessary cause. We must, therefore, never be too much absorbed by the thought we are pursuing, nor deceive ourselves about the value of our ideas or scientific theories ; we must always keep our eyes open for every event, the mind doubting and independent (p. 80), ready to study whatever presents itself and to let nothing go without seeking its reason. In a word,

• Claude Bernard, 8ur le mecanisme de la formation du sucre dans le foie {Comptes rendus par VAcad. des sciences, Sept. 24, 1855, and Comptes rendus de VAcad. des sciences, March 23, 1857). we must be in an intellectual attitude which seems paradoxical but which, in my opinion, expresses the true spirit of an investigator. We must have robust faith and not believe. Let me explain myself by saying that in science we must firmly believe in principles, but must question formulae; on the one hand, indeed, we are sure that determinism exists, but we are never certain we have attained it. We must be immovable as to the principles of experimental science (determinism), but must not absolutely believe in theories. The aphorism which I just uttered is sustained by what we expounded elsewhere (p. 67), to wit, that for experimental science principles are in our mind, while formulae are external things. In practical matters, we are indeed forced to tolerate the belief that truth (at least temporary truth) is embodied in a theory or a formula. But in scientific experimental philosophy those who put their faith in formulae and theories are wrong. All human science consists in seeking the true formula and true theory. We are always approaching it; but shall we ever find it completely? This is not the place to go into an explanation of philosophic ideas : let us return to our subject and pass on to a fresh experimental example.

Third example. — About the year 1852, my studies led me to make experiments on the influence of the nervous system on the phenomena of nutrition and temperature regulation. It had been observed in many cases that complex paralyses with their seat in the mixed nerves are followed, now by a rise and again by a fall of temperature in the paralyzed parts. !Now this is how I reasoned, in order to explain this fact, basing myself first on known observations and then on prevailing theories of the phenomena of nutrition and temperature regulation. Paralysis of the nerves, said I, should lead to cooling of the parts by slowing down the phenomena of combustion in the blood, since these phenomena are considered as the cause of animal heat. On the other hand, anatomists long ago noticed that the sympathetic nerves especially follow the arteries. So, thought I inductively, in a lesion of a mixed trunk of nerves, it must be the sympathetic nerves that produce the slowing down of chemical phenomena in capillary vessels, and their paralysis that then leads to cooling the parts. If my hypothesis is true, I went on, it can be verified by severing only the sympathetic, vascular nerves leading to a special part, and sparing the others. I should then find the part cooled by paralysis of the vascular nerves, without loss of

either motion or sensation, since the ordinary motor and sensory nerves would still be intact. To carry out my experiment, I therefore sought a suitable experimental method that would allow me to sever only the vascular nerves and to spare the others. Here the choice of animals was important in solving the problem (p. 122) ; for in certain animals, such as rabbits and horses, I found that the anatomical arrangement isolating the cervical sympathetic nerve made this solution possible.

Accordingly, I severed the cervical sympathetic nerve in the neck of a rabbit, to control my hypothesis and see what would happen in the way of change of temperature on the side of the head where this nerve branches out. On the basis of a prevailing theory and of earlier observation, I had been led, as we have just seen, to make the hypothesis that the temperature should be reduced. Now what happened was exactly the reverse. After severing the cervical sympathetic nerve about the middle of the neck, I immediately saw in the whole of the corresponding side of the rabbit's head a striking hyperactivity in the circulation, accompanied by increase of warmth. The result was therefore precisely the reverse of what my hypothesis, deduced from theory, had led me to expect; thereupon I did as I always do, that is to say, I at once abandoned theories and hypothesis, to observe and study the fact itself, so as to define the experimental conditions as precisely as possible. To-day my experiments on the vascular and thermo-regulatory nerves have opened a new path for investigation and are the subject of numerous studies which, I hope, may some day yield really important results in physiology and pathology.^ This example, like the preceding ones, proves that in experiments we may meet with results different from what theories and hypothesis lead us to expect. But I wish to call more special attention to this third example, because it gives us an important lesson, to wit : without the original guiding hypothesis, the experimental fact which contradicted it would never have been perceived. Indeed, I was not the first experimenter to cut this part of the cervical sympathetic nerve in living animals. Pourfour du Petit performed the experiment at the beginning of the last century and discovered the

• Claude Bernard, Reoherches expSrimentales stir le grand sympathique, etc. {M^moirea de la 8oci6t6 de hiologie, Vol. V, 1853). 8ur les nerfs vasoulaires et caloriques du grand sympathique {Comptes rendus de VAcad. des sciences, 1852, Vol. XXXIV; 1862, Vol. LV). nerve's action on the pupil, by starting from an anatomical hypothesis according to which this nerve was supposed to carry animal spirits to the eye.-^^ Many physiologists have since repeated the same operation, with the purpose of verifying or explaining the changes in the eye which Pourfour du Petit first described. But none of them noticed the local temperature phenomenon, of which I speak, or connected it with the severing of the cervical sympathetic nerve, though this phenomenon must necessarily have occurred under the very eyes of all who, before me, had cut this part of the sympathetic nerve. The hypothesis, as we see, had prepared my mind for seeing things in a certain direction, given by the hypothesis itself; and this is proved by the fact that, like the other experimenters, I myself had often divided the cervical sympathetic nerve to repeat Pourfour du Petit's experiment, without perceiving the fact of heat production which I later discovered when an hypothesis led me to make investigations in this direction. Here, therefore, the influence of the hypothesis could hardly be more evident ; we had the fact under our eyes and did not see it because it conveyed nothing to our mind. However, it could hardly be simpler to perceive, and since I described it, every physiologist without exception has noted and verified it with the greatest ease.

To sum up, even mistaken hypotheses and theories are of use in leading to discoveries. This remark is true in all the sciences. The alchemists founded chemistry by pursuing chimerical problems and theories which are false. In physical science, which is more advanced than biology, we might still cite men of science who make great discoveries by relying on false theories. It seems, indeed, a necessary weakness of our mind to be able to reach truth only across a multitude of errors and obstacles.

What general conclusions shall physiologists draw from the above examples? They should conclude that in the present state of biological science accepted ideas and theories embody only limited and risky truths which are destined to perish. They should consequently have very little confidence in the ultimate value of theories, but should still make use of them as intellectual tools necessary to the evolution of science and suitable for the discovery of new facts.

" Pourfour du Petit, Memoire dans lequel il est d4montrS que les nerfs intercostaux fournissent des rameaux qui portent des esprits dans les yeux {Histoire de VAcad4mie pour VannSe 1727). The art of discovering new phenomena and of noting them accurately should to-day be the special concern of all biologists. We must establish experimental criticism by creating rigorous methods of investigation and experimentation, which will enable us to define our observations unquestionably, and thus get rid of the errors of fact which are the source of errors in theory. A man who to-day attempted a generalization for biology as a whole would prove that he had no accurate feeling for the present state of the science. To-day, the biological problem has hardly begun to be put ; and, as stones must first be got together and cut, before we dream of erecting a monument, just so must the facts first be got together and prepared which are destined to create the science of living bodies. This role falls to experimentation ; its method is fixed, but the phenomena to be analyzed are so complex that, for the moment, the true promoters of science are those who succeed in giving its methods of analysis a few principles of simplification or in introducing improvements in instruments of research. When there are enough quite clearly established facts, generalizations never keep us waiting. I am convinced that, in experimental sciences that are evolving, and especially in those as complex as biology, discovery of a new tool for observation or experiment is much more useful than any number of systematic or philosophic dissertations. Indeed, a new method or a new means of investigation increases our power and makes discoveries and researches possible which would not have been possible without its help. Thus researches as to the formation of sugar in animals could be made only after chemistry gave us reagents for recognizing sugar, which were much more sensitive than those we had before.

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 pur 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 formulae 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.

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 phenomena. 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.)

These criticisms are all ill founded and completely violate the * F. A. Longet, Recherches cliniquea et expSrimentales sur lea fonctions des faisceaux de la moelle 4piniere et des racines des nerfs rachidiens, prSc^ddes d'un Examen historique et critique des experiences fait.es sur ces organes depuis Sir Ch. Bellf et suivies d'autres recherches sur diverses parties du systeme nerveux {Archives generates de midecine, 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 College 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 VAcademie des sciences, Vol. VIII, p. 787, June 3 and 10; Comptes rendus de VAcademie des sciences, June 4; Gazette des hdpitauXy 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 1839 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, d 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.

should we be mistaken ? Shall we say that our senses played us false at one period and not the other ? In that event we must give up experimentation; for the first requirement of experimenters is confidence in their senses and never any doubt except as to interpretations. If we cannot find the concrete reason for an error, despite all our efforts and all our investigations, we must suspend judgment and meantime keep both results; but never believe that denying positive facts can suffice even in the name of more numerous negative facts, or vice versa. NTegative facts, no matter how numerous they may be, can never destroy a single positive fact. That is why pure and simple negation is not criticism, and this method should be absolutely rejected in science, because science is never built up by negation.

To sum up, we must maintain the conviction that negative facts are determined like positive facts. We posited the principle that all experiments are successful, in that their conditions are determined ; in research into the conditions of each of these determinations lie the lessons that teach us the law of a phenomenon ; because in this way we learn the conditions necessary to its existence and its non-existence. After witnessing Magendie's experiments in 1839 and M, Longet's discussions in 1841, I have made this principle my guide, when I wished to take account of the phenomena myself and to judge the differences. I repeated the experiments, and, like Magendie and like M. Longet, I found cases of sensitivity and cases of insensitivity of the anterior spinal roots ; but as I was convinced that the two cases depended on different experimental conditions, I tried to define the conditions ; by dint of observation and perseverance, I finally found * the conditions in which we must place ourselves to get both results. Now that the conditions of the phenomenon are known, it is no longer questioned. M. Longet himself ^ and all physiologists accept the fact of recurrent sensitivity as constant in the conditions which I announced.

From what has gone before, we must therefore establish the absolute and necessary determination of phenomena as a principle of experimental criticism. This principle, when thoroughly understood, should make us cautious about our natural tendency to contradic- * Claude Bernard, Lecons sur la physiologic et la pathologic du syatdme nerveuxy p. 32. tion. Certainly every experimenter, especially every beginner, feels a secret pleasure whenever he finds something different from what others have seen before him. His first impulse is to contradict, especially when contradicting someone high in the scientific world. We must protect ourselves against this tendency, for it is not scientific. Pure contradiction would amount to an accusation of lying, and we should avoid it because happily scientific falsifiers are rare. As such cases, moreover, have no connection with science, I need not offer any precept on the subject. I wish merely to point out here that science does not consist in proving that others are mistaken; and even if we proved that an eminent man was mistaken, that would not be a great discovery ; it can be a profitable work for science only in so far as we show how he was mistaken. Indeed, great men often teach us by their errors as much as by their discoveries. I sometimes hear it said that pointing out an error is equivalent to a discovery. Yes, on condition that we bring to light a new truth by showing the source of error, in which event it is unnecessary to combat the error; it falls of itself. Thus only is criticism equivalent to a discovery; when it explains everything without denying anything and finds the correct causation of apparently contradictory facts. By such determinism everything is unified, everything becomes transparent ; and as Leibnitz says, science, as it broadens, grows clear and simple.

II. The Principle of Determinism Ejects Causeless and Irrational Facts from Science We said elsewhere (p. 54) that our reason scientifically includes the determinate and the indeterminate but that it cannot accept the indeterminable, because that would be nothing but accepting the marvellous, occult or supernatural which should be absolutely banished from all experimental science. The result is that a fact gains scientific value only through knowledge of its causation. A crude fact is not scientific, and a fact whose causation is irrational should also be ejected from science. Indeed, if an experimenter must submit his ideas to the criterion of facts, I do not acknowledge that he must submit his reason ; for then he would extinguish the torch of his inner criterion and would necessarily fall into the realm of the indeterminable, i.e., the occult and the marvellous. In science, many crude

facts are doubtless still incomprehensible; I do not mean to conclude that we should willfully reject all these facts, I wish simply to say that they should be held in reserve, for a time, as crude facts, and not introduced into science, i.e., into experimental reasoning, until their necessary conditions are defined in terms of rational determinism. Otherwise, our experimental reasoning would be continually halted or else inevitably led into the absurd.

The following examples, among many others, will prove what I assert. First example. — A few years ago,^ I experimented on the influence of ether on intestinal secretions. Now a propos of this, I happened to observe that injecting ether into the intestinal canal of a dog kept without food even for several days gave rise to splendid white lymphatics, absolutely like those in an animal actively digesting mixed food in which there is fat. After frequent repetitions, the fact was unquestionable. But what meaning could be ascribed to it ? What reasoning was possible about its cause ? Should we say : ether causes secretion of chyme? This is a fact. But that would be absurd, since there was no food in the intestine. As we see, reason rejected this causation as irrational and absurd in our present state of knowledge. I therefore tried to find the reason for this incomprehensible fact, and I finally saw that there was a source of error, because the ether dissolved the oil lubricating the piston of the syringe with which it was injected into the stomach; when the ether was injected with a glass pipette, instead of a syringe, it no longer produced the phenomenon. The irrationality of the fact, therefore, led me to see a priori that it must be false, and that it could not be used as a basis for scientific reasoning. Otherwise I should not have found the curious source of error located in the piston of a syringe. But when the source of error was once recognized, everything was explained, and the fact became rational in this sense, that the chyle was produced there, as everywhere else, by the absorption of fat ; only the ether stimulated absorption and made the phenomenon more evident.

• Claude Bernard, LeQons sur lea ejfets des substances toxiques et m^dicamenteuses, p. 428. that the venom of a toad speedily poisons frogs and other animals, while it has no effect on the toad himself. Here, in fact, is a quite simple experiment that seems to prove it : if we take venom on a lancet from the parotid glands of a domestic toad and insert it under the skin of a frog or a bird, the animals soon perish ; while if we insert the same amount of venom under the skin of a toad of about the same size, he does not die of it, indeed he feels no effect. Here again is a crude fact which could become scientific only on condition that we learn how venom acts on a frog, and why it does not act on a toad. To do this, I necessarily studied the mechanism of death, for special circumstances might be encountered which would explain the difference in results on the frog and on the toad. Thus a special arrangement of the nostrils and the epiglottis explains very well why, for example, section of the two facial nerves is mortal in horses and not in other animals. But this exceptional fact is rational ; it confirms the rule, as we say, in that it makes no change fundamentally in the nervous paralysis which is the same in all animals. There was nothing of the kind in the case with which we are concerned : study of the mechanism of death by toad's venom led to the conclusion that toad's venom kills by stopping the heart in frogs, while it does not act on a toad's heart. Now, in logic, we should necessarily have to admit that the muscular fibres of a toad's heart have a different nature from those of a frog's heart, since the poison which acts on the former does not act on the latter.

That was impossible: for admitting that organic units identical in structure and in physiological characteristics are no longer identical in the presence of a toxic action identically the same would prove that phenomena have no necessary causation ; and thus science would be denied. Pursuant to these ideas, I rejected the above-mentioned fact as irrational, and decided to repeat the experiments, even though I did not doubt their accuracy as crude fact^ I then saw ® that toad's venom easily kills frogs with a dose that is wholly insufficient for a toad, but that the latter is nevertheless poisoned if we increase the dose enough. So that the difference described was reduced to a question of quantity and did not have the contradictory meaning that might be ascribed to it. The irrationality of the fact was, therefore, again what led me to ascribe to it another meaning.

'Claude Bernard, Coura de pathologic exp^rimentale (Medical Times, 1860). We have just seen that our reason forces us to reject apparently causeless facts and leads us to criticise them so as to find for them a rational meaning before using them in experimental reasoning. But since criticism, as we said, rests at once on reason and on philosophic doubt, it follows that a simple and logical appearance is not enough to make us accept an experimental fact; we should still doubt and by a counter experiment should see whether the rational appearance is not misleading. This is an absolutely strict precept, especially in medical science which by its complexity conceals additional sources of error. I have elsewhere (p. 55) described the experimental character of counterproof s ; I will not return to that subject; I wish merely to point out here that, even when a fact seems logical, i.e., rational, we are never justified in omitting a counterproof or counter experiment, so that I consider this precept a kind of order which we must blindly follow even in cases which seem the clearest and most rational. I am going to quote two examples which will show the necessity of thus making a comparative experiment always and in spite of everything.

First example. — I explained before (p. 164) how I was once led to study the part played by sugar in nutrition and to investigate the mechanism by which this nutritive principle was destroyed in the organism. To solve this problem, I had to hunt for sugar in the blood and follow it into the intestinal vessels which absorbed it, until I could note the place where it disappeared. To carry out my experiment, I gave a dog sweetened milk soup ; then I sacrificed the animal during digestion and found that the blood in the superhepatic vessels, which hold all the blood of the intestinal organs and the liver, contained sugar. It was quite natural and, as we say, logical to think that the sugar found in the superhepatic vessels was the same that 1 had given the animal in his soup. I am certain indeed that more than one experimenter would have stopped at that and would have considered it superfluous, if not ridiculous, to make a comparative experiment. However, I made a comparative experiment, because I was convinced of its absolute necessity on principle: which means that I am convinced that we must always doubt in physiology, even in cases where doubt seems least allowable. However, I must add