An Introduction to the Study of Experimental Medicine

Third example. — In 1857, I undertook a series of experiments on the elimination of substances in the urine, and this time the results of the experiment, unlike the previous examples, did not confirm my previsions or preconceived ideas. I had therefore made what we habitually call an unsuccessful experiment. But we have already posited the principle that there are no unsuccessful experiments; for, when they do not serve the investigation for which they were devised, we must still profit by observation to find occasion for other experiments.

In investigating how the blood, leaving the kidney, eliminated substances that I had injected, I chanced to observe that the blood in the renal vein was crimson, while the blood in the neighboring veins was dark like ordinary venous blood. This unexpected peculiarity struck me, and I thus made observation of a fresh fact begotten by the experiment, but foreign to the experimental aim pursued at the moment. I therefore gave up my unverified original idea, and directed my attention to the singular coloring of the venous renal blood ; and when I had noted it well and assured myself that there was no source of error in my observation, I naturally asked myself what could be its cause. As I examined the urine flowing through the urethra and reflected about it, it occurred to me that the red coloring of the venous blood might well be connected with the secreting or active state of the kidney. On this hypothesis, if the renal secretion was stopped, the venous blood should become dark : that is what

happened; when the renal secretion was reestablished, the venous blood should become crimson again ; this I also succeeded in verifying whenever I excited the secretion of urine. I thus secured experimental proof that there is a connection between the secretion of urine and the coloring of blood in the renal vein. But that is still by no means all. In the normal state, venous blood in the kidney is almost constantly crimson, because the urinary organ secretes almost continuously, though alternately for each kidney. Now I wished to know whether the crimson color is a general fact characteristic of the other glands, and in this way to get a clear-cut counterproof demonstrating that the phenomenon of secretion itself was what led to the alteration in the color of the venous blood. I reasoned thus : if, said I, secretion, as it seems to be, causes the crimson color of glandular venous blood, then, in such glandular organs as the salivary glands which secrete intermittently, the venous blood will change color intermittently and become dark, while the gland is at rest, and red during secretion. So I uncovered a dog's submaxillary gland, its ducts, its nerves and its vessels. In its normal state, this gland supplies an intermittent secretion which we can excite or stop at pleasure. ^Tow while the gland was at rest, and nothing flowed through the salivary duct, I clearly noted that the venous blood was, indeed, dark, while, as soon as secretion appeared, the blood became crimson, to resume its dark color when the secretion stopped; and it remained dark as long as the intermission lasted, etc.^

These last observations later became the starting point for new ideas which guided me in making investigations as to the chemical cause of the change in color of glandular blood during secretion. I shall not further describe these experiments which, moreover, I have published in detail.^ It is enough for me to prove that scientific investigations and experimental ideas may have their birth in almost involuntary chance observations which present themselves either spontaneously or in an experiment made with a different purpose.

' Claude Bernard, Legons sur les proprietes physiologiques et les alterations pathologiques des liquides de Vorganisme. Paris, 1859. Vol. II. • Claude Bernard, Sur la quantity d'oxygene que contient le sang veineuw des organes glandulaires. {Compt. rend, de VAcad. des sciences. Vol. XL VII, Sept. 6, 1858.) Let me cite another case, — one in which, an experimenter produces an observation and voluntarily brings it to birth. This case is, so to speak, included in the preceding case ; but it differs from it in this, that, instead of waiting for an observation to present itself by chance in fortuitous circumstances, we produce it by experiment. Returning to Bacon's comparison, we might say that an experimenter, in this instance, is like a hunter who, instead of waiting quietly for game, tries to make it rise, by beating up the locality where he assumes it is. We use this method whenever we have no preconceived idea in respect to a subject as to which previous observations are lacking. So we experiment to bring to birth observations which in turn may bring to birth ideas. This continually occurs in medicine when we wish to^ investigate the action of a poison or of some medicinal substance, on an animal's economy; we make experiments to see, and we then take our direction from what we have seen.

Fourth example. — In 1845, Monsieur Pelouze gave me a toxic substance, called curarej which had been brought to him from America. We then knew nothing about the physiological action of this substance. From old observations and from the interesting accounts of Alex, von Humboldt and of Roulin and Boussingault, we knew only that the preparation of this substance was complex and difficult, and that it very speedily kills an animal if introduced under the skin. But from the earlier observations, I could get no idea of the mechanism of death by curare ; to get such an idea I had to make fresh observations as to the organic disturbances to which this poison might lead. I therefore made experiments to see things about which I had absolutely no preconceived idea. First, I put curare under the skin of a frog : it died after a few minutes ; I opened it at once, and in this physiological autopsy I studied in succession what had become of the known physiological properties of its various tissues. I say physiological autopsy purposely, because no others are really instructive. The disappearance of physiological properties is what explains death, and not anatomical changes. Indeed, in the present state of science, we see physiological properties disappear in any number of cases without being able to show, by our present means of observation, any corresponding anatomical change; such, for example, is the case with curare. Meantime, we shall find examples, on the contrary, in which physiological properties persist, in spite of very marked anatomical changes with which the functions are by

no means incompatible. Now in my frog poisoned with curare, the heart maintained its movements, the blood was apparently no more changed in physiological properties than the muscles, which kept their normal contractility. But while the nervous system had kept its normal anatomical appearance, the properties of the nerves had nevertheless completely disappeared. There were no movements, either voluntary or reflex, and when the motor nerves were stimulated directly, they no longer caused any contraction in the muscles. To learn whether there was anything accidental or mistaken in this first observation, I repeated it several times and verified it in various ways; for when we wish to reason experimentally, the first thing necessary is to be a good observer and to make quite certain that the starting point of our reasoning is not a mistake in observation. In mammals and in birds, I found the same phenomena as in frogs, and disappearance of the physiological properties of the motor nervous system became my constant fact. Starting from this well established fact, I could then carry analysis of the phenomena further and determine the mechanism of death from curare. I still proceeded by reasonings analogous to those quoted in the above example, and, from idea to idea and experiment to experiment, I progressed to more and more definite facts. I finally reached this general proposition, that curare causes death by destroying all the motor nerves, without affecting the sensory neirves^

In cases where we make an experiment in which both preconceived idea and reasoning seem completely lacking, we yet necessarily reason by syllogism without knowing it. In the case of curare, I instinctively reasoned in the following way : no phenomenon is without a cause, and consequently no poisoning without a physiological lesion peculiar or proper to the poison used ; now, thought I, curare must cause death by an activity special to itself and by acting on certain definite organic parts. So by poisoning an animal with curare and by examining the properties of its various tissues immediately after death, I can perhaps find and study the lesions peculiar to it.

The mind, then, is still active here, and an experiment in order to see is included, nevertheless, in our general definition of an experiment (p. 10). In every enterprise, in fact, the mind is always rea- Cf. Claude Bernard, Legons sur les effets des substances toxiquea; Paris, 1857 J Du curare. {Revue des Deuw Mondes, Sept. 1, 1864.) soning, and, even when we seem to act without a motive, an instinctive logic still directs the mind. Only we are not aware of it, because we begin by reasoning before we know or say that we are reasoning, just as we begin by speaking before we observe that we are speaking, and just as we begin by seeing and hearing before we know what we see or what we hear.

Fifth example. — About 1846, I wished to make experiments on the cause of poisoning with carbon monoxide. I knew that this gas had been described as toxic, but I knew literally nothing about the mechanism of its poisoning; I therefore could not have a preconceived opinion. What, then, was to be done? I must bring to birth an idea by making a fact appear, i.e., make another experiment to see. In fact I poisoned a dog by making him breathe carbon monoxide and after death I at once opened his body. I looked at the state of the organs and fluids. What caught my attention at once was that its blood was scarlet in all the vessels, in the veins as well as the arteries, in the right heart as well as in the left. I repeated the experiment on rabbits, birds and frogs, and everywhere I found the same scarlet coloring of the blood. But I was diverted from continuing this investigation, and I kept this observation a long time unused except for quoting it in my course a propos of the coloring of blood.

In 1856, no one had carried the experimental question further, and in my course at the College de France on toxic and medicinal substances, I again took up the study of poisoning by carbon monoxide which I had begun in 1846. I found myself then in a confused situation, for at this time I already knew that poisoning with carbon monoxide makes the blood scarlet in the whole circulatorv system. I had to make hypotheses, and establish a preconceived idea about my first observation, so as to go ahead. Now, reflecting on the fact of scarlet blood, I tried to interpret it by my earlier knowledge as to the cause of the color of blood. Whereupon all the following reflections presented themselves to my mind. The scarlet color, said I, is peculiar to arterial blood and connected with the presence of a large proportion of oxygen, while dark coloring belongs with absence of oxygen and presence of a larger proportion of carbonic acid ; so the idea occurred to me that carbon monoxide, by keeping venous blood scarlet, might perhaps have prevented the oxygen from changing into carbonic acid in the capillaries. Yet

it seemed hard to understand how that could be the cause of death. But still keeping on with my inner preconceived reasoning, I added : If that is true, blood taken from the veins of animals poisoned with carbon monoxide should be like arterial blood in containing oxygen ; we must see if that is the fact. Following this reasoning, based on interpretation of my observation, I tried an experiment to verify my hypothesis as to the persistence of oxygen in the venous blood. I passed a current of hydrogen through scarlet venous blood taken from an animal poisoned with carbon monoxide, but I could not liberate the oxygen as usual. I tried to do the same with arterial blood; I had no greater success. My preconceived idea was therefore false. But the impossibility of getting oxygen from the blood of a dog poisoned with carbon monoxide was a second observation which suggested a fresh hypothesis. What could have become of the oxygen in the blood? It had not changed into carbonic acid, because I had not set free large quantities of that gas in passing a current of hydrogen through the blood of the poisoned animals. Moreover, that hypothesis was contrary to the color of the blood. I exhausted myself in conjectures about how carbon monoxide could cause the oxygen to disappear from the blood ; and as gases displace one another I naturally thought that the carbon monoxide might have displaced the oxygen and driven it out of the blood. To learn this, I decided to vary my experimentation by putting the blood in artificial conditions that would allow me to recover the displaced oxygen. So I studied the action of carbon monoxide on blood experimentally. Tor this purpose I took a certain amount of arterial blood from a healthy animal ; I put this blood on the mercury in an inverted test tube containing carbon monoxide; I then shook the whole thing so as to poison tlie blood sheltered from contact with the outer air.

Then, after an interval, I examined whether the air in the test-tube in contact with the poisoned blood had been changed, and I noted that the air thus in contact with the blood had been remarkably enriched with oxygen, while the proportion of carbon monoxide was lessened. Repeated in the same conditions, these experiments taught me that what had occurred was an exchange, volume by volume, between the carbon monoxide and the oxygen of the blood. But the carbon monoxide, in displacing the oxygen that it had expelled from the blood, remained chemically combined in the blood and could no longer be displaced

either by oxygen or by other gases. So that death came through death of the molecules of blood, or in other words by stopping their exercise of a physiological property essential to life. This last example, which I have very briefly described, is complete; it shows from one end to the other, how we proceed with the experimental method and succeeded in learning the immediate cause of phenomena. To begin with I knew literally nothing about the mechanism of the phenomenon of poisoning with carbon monoxide. I undertook an experiment to see, i.e., to observe. I made a preliminary observation of a special change in the coloring of blood. I interpreted this observation, and I made an hypothesis which proved false. But the experiment provided me with a second observation about which I reasoned anew, using it as a starting point for making a new hypothesis as to the mechanism, by which the oxygen in the blood was removed. By building up hypotheses, one by one, about the facts as I observed them, I finally succeeded in showing that carbon monoxide replaces oxygen in a molecule of blood, by combining with the substance of the molecule. Experimental analysis, here, has reached its goal. This is one of the cases, rare in physiology, which I am happy to be able to quote. Here the immediate cause of the phenomenon of poisoning is found and is translated into a theory which accounts for all the facts and at the same time includes all the observations and experiments. Formulated as follows, the theory posits the main facts from which all the rest are deduced : Carbon monoxide combines more intimately than oxygen with the hemoglobin in a molecule of blood. It has quite recently been proved that carbon monoxide forms a definite combination with hemoglobin.^ So that the molecule of blood, as if petrified by the stability of the combination, loses its vital properties.

Hence everything is logically deduced: because of its property of more intimate combination, carbon monoxide drives out of the blood the oxygen essential to life ; the molecules of blood become inert, and the animal dies, with symptoms of hemorrhage, from true paralysis of the molecules. But when a theory is sound and indeed shows the real and definite physico-chemical cause of phenomena, it not only includes the observed facts but predicts others and leads to rational applications that are logical consequences of the theory. Here again we

' Hoppe-Seyler, Handbuch der physiologischund pathologisich-chemischen Analyse. Berlin, 1865. meet this criterion. In fact, if carbon monoxide has the property of driving out oxygen by taking its place in combining with a molecule of blood, we should be able to use the gas to analyze the gases in blood, and especially for determining oxygen. From my experiments I deduced this application which has been generally adopted to-day.^ Applications of this property of carbon monoxide have been made in legal medicine for finding the coloring matter of blood ; and from the physiological facts described above we may also already deduce results connected with hygiene, experimental pathology, and notably with the mechanism of certain forms of anemia.

As in every other case, all the deductions from the theory doubtless still require experimental verification; and logic does not suffice. But this is because the conditions in which carbon monoxide acts on the blood may present other complex circumstances and any number of details which the theory cannot yet predict. Otherwise, as we have often said (p. 29), we could reach conclusions by logic alone, without any need of experimental verifications. Because of possible unforeseen and variable new elements in the conditions of a phenomenon, logic alone can in experimental science never sufiice. Even when we have a theory that seems sound, it is never more than relatively sound, and it always includes a certain proportion of the unknown.

We have already said (p. 25) and we shall see further on, that in noting an observation we must never go beyond facts. But in making an experiment, it is different. I wish to show that hypotheses are indispensable, and that they are useful, therefore, precisely because they lead us outside of facts and carry science forward. The object of hypotheses is not only to make us try new experiments ; they also often make us discover new facts which we should not have perceived without them. In the preceding examples, we saw that we can start from a particular fact and rise one by one to more general ideas, i.e., to a theory. But as we have just seen, we can also sometimes

• Claude Bernard, De Vemploi de Voxyde de carhone pour la determination de Voxygdne du sang {Compt. rend, de VAcad. des sciences, Meeting of Sept. 6, 1858, Vol. XLVII). start with an hypothesis deduced from a theory. Though we are dealing in this case with reasoning logically deduced from a theory, we have an hypothesis that must still be verified by experiment. Indeed, theories are only an assembling of the earlier facts, on which our hypothesis rests, and cannot be used to demonstrate it experimentally. We said that, in this instance, we must not submit to the yoke of theories, and that keeping our mental independence is the best way to discover the truth. This is proved by the following examples.

First example. — In 1843, in one of my first pieces of work, 1 undertook to study what becomes of different alimentary substances in nutrition. As I said before, I began with sugar, a definite substance that is easier than any other to recognize and follow in the bodily economy. With this in view, I injected solutions of cane sugar into the blood of animals, and I noted that even when injected in weak doses the sugar passed into the urine. I recognized later that, by changing or transforming sugar, the gastric juice made it capable of assimilation, i.e., of destruction in the blood.^

Thereupon I wished to learn in what organ the nutritive sugar disappeared, and I conceived the hypothesis that sugar introduced into the blood through nutrition might be destroyed in the lungs or in the general capillaries. The theory, indeed, which then prevailed and which was naturally my proper starting point, assumed that the sugar present in animals came exclusively from foods, and that it was destroyed in animal organisms by the phenomena of combustion, i.e., of respiration. Thus sugar had gained the name of respiratory nutriment. But I was immediately led to see that the theory about the origin of sugar in animals, which served me as a starting point, was false. As a result of the experiments which I shall describe further on, I was not indeed led to find an organ for destroying sugar, but, on the contrary, I discovered an organ for making it, and I found that all animal blood contains sugar even when they do not eat it. So I noted a new fact, unforeseen in theory, which men had not noticed, doubtless because they were under the influence of contrary theories which they had too confidently accepted. I therefore abandoned my hypothesis on the spot, so as to pursue the unexpected result which has since become the fertile * Claude Bernard, Thesis for doctorate in medicine, Paris, 1843.

origin of a new path for investigation and a mine of discoveries that is not yet exhausted. In these researches I followed the principles of the experimental method that we have established, i.e., that, in presence of a well-noted, new fact which contradicts a theory, instead of keeping the theory and abandoning the fact, I should keep and study the fact, and I hastened to give up the theory, thus conforming to the precept which we proposed in the second chapter: ^^When we meet a fact which contradicts a prevailing theory, we must accept the fact and abandon the theory, even when the theory is supported by great names and generally accepted.''

We must therefore distinguish, as we said, between principles and theories, and never believe absolutely in the latter. We had a theory here which assumed that the vegetable kingdom alone had the power of creating the individual compounds which the animal kingdom is supposed to destroy. According to this theory, established and supported by the most illustrious chemists of our day, animals were incapable of producing sugar in their organisms. If I had believed in this theory absolutely, I should have had to conclude that my experiment was vitiated by some inaccuracy; and less wary experimenters than I might have condemned it at once, and might not have tarried longer at an observation which could be theoretically suspected of including sources of error, since it showed sugar in the blood of animals on a diet that lacked starchy or sugary materials. But instead of being concerned about the theory, I concerned myself only with the fact whose reality I was trying to establish. By new experiments and by means of suitable counterproofs, I was thus led to confirm my first observation and to find that the liver is the organ in which animal sugar is formed in certain given circumstances, to spread later into the whole blood supply and into the tissues and fluids.

Animal glycogenesis which I thus discovered, i.e., the power of producing sugar, possessed by animals as well as vegetables, is now an acquired fact for science ; but we have not yet fixed on a plausible theory accounting for the phenomenon. The fresh facts which I made known are the source of numerous studies and many varied theories in apparent contradiction with each other and with my own. When entering on new ground we must not be afraid to express even risky ideas so as to stimulate research in all directions. As Priestley

put it, we must not remain inactive through false modesty based on fear of being mistaken. So I made more or less hypothetical theories of glycogenesis ; after mine came others ; my theories, like other men^s, will live the allotted life of necessarily very partial and temporary theories at the opening of a new series of investigations ; they will be replaced later by others, embodying a more advanced stage of the question, and so on. Theories are like a stairway ; by climbing, science widens its horizon more and more, because theories embody and necessarily include proportionately more facts as they advance. Progress is achieved by exchanging our theories for new ones which go further than the old, until we find one based on a larger number of facts. In the case which now concerns us, the question is not one of condemning the old to the advantage of a more recent theory. What is important is having opened a new road ; for well-observed facts, though brought to light by passing theories, will never die; they are the material on which alone the house of science will at last be built, when it has facts enough and has gone sufficientlj^ deep into the analysis of phenomena to know their law or their causation.

To sum up, theories are only hypotheses, verified by more or less numerous facts. Those verified by the most facts are the best; but even then they are never final, never to be absolutely believed. We have seen in the preceding examples that if we had had complete confidence in the prevailing theory of the destruction of sugar in animals, and if we had only had its confirmation in view, we should probably not have found the road to the new facts which we met. It is true that an hypothesis based on a theory produced the experiment ; but as soon as the results of the experiment appeared, theory and hypothesis had to disappear, for the experimental facts were now just an observation, to be made without any preconceived idea (p. 21).

In sciences as complex and as little developed as physiology, the great principle is therefore to give little heed to hypotheses or theories and always to keep an eye alert to observe everything that appears in every aspect of an experiment. An apparently accidental and inexplicable circumstance may occasion the discovery of an important new fact, as we shall see in the continuation of the example just noted. Second example (Sequel to the Last). — After finding, as I said above, that there is sugar in the livers of animals in their normal state, and with every sort of nutriment, I wished to learn the pro-

portion of this substance and its variation in certain physiological and pathological states. So I began to estimate the sugar in the livers of animals placed in various physiologically defined circumstances. I always made two determinations of carbohydrate for the same liver tissue. But pressed for time one day, it happened that I could not make my two analyses at the same moment ; I quickly made one determination just after the animal's death and postponed the other analysis till next day. But then I found much larger amounts of sugar than those which I got the night before with the same material. I noticed, on the other hand, that the proportion of sugar, which I had found just after the animaPs death the night before, was much smaller than I had found in the experiments which I had announced as giving the normal proportion of liver sugar. I did not know how to account for this singular variation, got with the same liver and the same method of analysis. What was to be done ? Should I consider two such discordant determinations as an unsuccessful experiment and take no account of them ? Should I take the mean between these experiments ? More than one experimenter might have chosen this expedient to get out of an awkward situation. But I disapprove of this kind of action for reasons which I have given elsewhere. I said, indeed, that we must never neglect anything in our observation of fact, and I consider it indispensable, never to admit the existence of an unproved source of error in an experiment and always to try to find a reason for the abnormal circumstances that we observe. Nothing is accidental, and what seems to us accident is only an unknown fact whose explanation may furnish the occasion for a more or less important discovery. So it proved in this case.

I wished, in fact, to learn the reason for my having found two such different values in the analysis of my rabbit's liver. After assuring myself that there was no mistake connected with the method of analysis, after noting that all parts of the liver were practically equally rich in sugar, there remained to be studied only the elapsed time between the animal's death and the time of my second determination. Without ascribing much importance to it, up to that time I had made my experiments a few hours after the animal's death; now for the first time I was in the situation of making one determination only a few minutes after death and postponing the other till next day, i.e., twenty-four hours later. In physiology, questions

of time are always very important because organic matter passes through numerous and incessant changes. Some chemical change might therefore have taken place in the liver tissue. To make sure, I made a series of new experiments which dispelled every obscurity by showing me that liver tissue becomes more and more rich in sugar for some time after death. Thus we may have a very variable amount of sugar according to the moment when we make our examination. I was therefore led to correct my old determination and to discover the new fact that considerable amounts of sugar are produced in animals' livers after death. For instance, by forcibly injecting a current of cold water through the hepatic vessels and passing it through a liver that was still warm, just after an animal's death, I showed that the tissue was completely freed from the sugar which it contained; but next day or a few hours later, if we keep the washed liver at a mild temperature, we again find its tissue charged with a large amount of sugar produced after it was washed.^