CLAUDE BERNARD

The spontaneity enjoyed by beings endowed with life has been one of the principal objections that has been raised against the use of experimentation in biological studies. Each living being, in effect, appears to us as if provided with a kind of interior force which presides over vital manifestations, which become more and more independent of the general influence of the cosmos, the more the being in question rises in the scale of organization. In the higher animals and in man, for example, this vital force appears to result in the withdrawal of the living body from general physico-chemical influences, and thus renders experimental access to it very difficult.

Many doctors and speculative physiologists, along with some anatomists and naturalists, have exploited these various arguments to protest against experimentation on living beings. They have supposed that the vital force was in opposition to the physico-chemical forces, and that this vital force dominated all the phenomena of life, subjecting them to altogether special laws, and making the organism an organized whole which the experimenter could not touch without destroying the very character of life itself. They have even gone so far as to say that inorganic bodies and living bodies differed radically from this point of view, in such a manner that experimentation was applicable to the one kind of body and not to the other. Cuvier, who shares this opinion, and who thinks that physiology should be a science of observation and of anatomical deduction, expresses himself thus: "All parts of a living body are connected; they can only act in so far as they all act together. Separating one part from the whole means sending it back to the realm of dead substances; it would change the essence of the body entirely." [6]

If the preceding objections had some foundation, we would have to acknowledge that either determinism is impossible in the phenomena of life-which would simply deny biological science-or that the vital force must be studied by particular procedures and that the science of life must rest on other principles than the science of inert bodies. These ideas, which were current in other time periods, are undoubtedly fading away now more and more; however, it is important to wipe out the final traces of them, because whatever remains of these so-called vitalist ideas in certain minds represents a real obstacle to the progress of experimental medicine.

I propose therefore to establish that the science of the phenomena of life must have the same basis as that of the science of inorganic bodies, and that there is no difference in this respect between the principles of the biological sciences and those of the physico-chemical sciences. In fact, just as we have said previously, the goal which the experimental method proposes is the same everywhere; it consists in reconnecting by experiment natural phenomena with their conditions of existence or to their immediate causes. In biology, these causes being known, the physiologist will be able to direct the manifestations of the phenomena of life just as the physicist and the chemist direct the natural phenomena whose laws they have discovered; but in doing this, the experimenter does not act on life.

It is very important, in order to understand completely the application of experimentation to living beings, to be perfectly clear about the ideas which we are developing at this point. When we examine a higher living organism, that is to say, a complex being, and when we observe it carrying out its different functions in the general cosmic environment common to all phenomena of nature, the organism seems independent of that environment up to a certain point. But this appearance results from our illusions concerning the simplicity of the phenomena of life. The external phenomena which we perceive in that living being are fundamentally very complex, and they represent the result of a host of intimate properties of organic elements whose manifestations are linked to the physico-chemical conditions of the internal environments in which these elements are immersed. In our explanations, we do away with this internal environment and only see the external environment which is before our eyes. But the real explanation of the phenomena of life rests on the study and knowledge of the most tenuous and subtle particles which form the organic elements of the body. This idea, set down in biology long ago by the great physiologists, appears more and more valid as the study of the organization of living beings makes greater progress. We must learn in addition that these intimate particles of the organization only manifest their vital activity by a necessary physicochemical relation with intimate environments which we should equally study and know. Otherwise, if we limit ourselves to the examination of the total phenomena visible from the outside, we might falsely believe that there is a unique force in living beings which violates the physicochemical laws of the general cosmic environment, in the same way an ignorant person could believe that there is a special force which violates the laws of gravity in a machine which mounts into the air or runs along the ground. Now a living organism is nothing but an amazing machine endowed with the most marvelous properties and activated by the aid of the most complex and delicate mechanisms. There are no opposing forces struggling with one another; nature only knows order and disorder, harmony and discord.

In experimentation on inorganic bodies, we only need to take into account a single environment, the external cosmic environment; while in higher living beings, there are at least two environments to consider: the external environment or extra-organic, and the internal environment [milieu intérieur] or intra-organic. Each year in my course on physiology in the Faculty of Sciences, I develop these new ideas on organic environments, ideas which I consider the basis of general physiology; they also necessarily form the basis of general pathology, and these same concepts will guide us in the application of experimentation to living beings. As I have said elsewhere, the complexity due to the existence of an organic internal environment is the only reason for the great difficulties which we encounter in the experimental determination of the phenomena; of life and in the application of the means capable of modifying these phenomena. [7]

With the aid of the thermometer, the barometer, and all the instruments which record and measure the properties of the external environment, the physicist and the chemist who experiment on inert bodies, having only to consider the external environment, can always set up identical conditions. For the physiologist, these instruments no longer suffice, and besides, it is in the milieu intérieur which he must employ them. In effect it is the milieu intérieur of living beings which is always in immediate relation with the normal or pathological vital manifestations of the organic elements. The higher one travels up the scale of living beings, the more the organization becomes more complicated, and the more the organic elements become more delicate and require a more perfect milieu intérieur. All the circulating fluids, the blood serum and the intraorganic fluids, in reality constitute this milieu intérieur.

In all living beings, the milieu intérieur, which is a true product of the organism, preserv es the necessary relations of exchange and equilibrium with the external cosmic environment; but, as the organism becomes more perfect, the organic environment becomes more specialized and in some manner isolates itself more and more from the ambient environment. In plants and coldblooded animals, as we have said before, this isolation is less complete than in hot-blooded animals; in hot-blooded animals, the blood maintains an almost fixed and constant temperature and composition. But these different conditions do not create differences in nature among different living beings; they only represent improvements in the environmental mechanisms of isolation and protection. The vital manifestations of animals only vary because the physicochemical conditions of their internal environments vary; thus a mammal whose blood has been cooled, either by natural hibernation, or by certain lesions of the nervous system, completely resembles, in the properties of its tissues, a true cold-blooded animal.

In sum, one can, according to what has been said, construct an idea of the enormous complexity of the phenomena of life and the almost insurmountable difficulties in exactly determining them which confront the physiologist when he is forced to carry out experimentation in these interior or organic environments. Nevertheless, these obstacles will not frighten us if we are convinced that we are travelling along the right path. In effect, there is an absolute determinism in all vital phenomena; hence there exists a biological science, and consequently, all the studies to which we devote ourselves will not be in vain. General physiology is the fundamental biological science towards which all the other biological sciences converge. Its main concern is to determine the elementary conditions of the phenomena of life. Pathology and therapeutics also rest on this common foundation. It is through the normal activity of the organic elements that life maintains a state of health; it is the abnormal manifestation of these same elements which characterizes disease, and in the end through the intermediary of the organic environment modified by the means of certain toxic or medicinal substances, therapeutics can act on the organic elements. To arrive at a resolution of these various problems, it is necessary to break down the organism successively, as one takes apart a machine in order to understand it and to study all the workings; this means, that before experimenting on the elements, it is first necessary to experiment on the apparatus and the organs. We must have recourse to a successive analytical study of the phenomena of life by using the same experimental method which the physicist and the chemist use to analyze the phenomena of inorganic bodies. The difficulties which result from the complexity of the phenomena of living bodies, arise solely in the application of experimentation, because in the end the goal and the principles of the method always remain exactly the same.

The ideas which we developed in the first two parts of this introduction will be better understood if we can apply them to investigations of physiology and experimental medicine and show that these ideas can serve as easily remembered precepts for experimenters. That is why I have brought together in what follows a certain number of examples which appeared most suitable to me in order to make my point. In all these examples, I have, as much as possible, cited my own work, for the sole reason that in the case of reasoning and intellectual processes, I will be much more certain about what I am advancing in describing what happened to me than what may have taken place in the minds of others. Besides, I do not presume to offer these examples as models to follow; I only employ them to express my ideas better and to make my thought easier to grasp.

Experimental ideas are often born by accident or on the occasion of a fortuitous observation. Nothing is more common, and this is the simplest way to begin a scientific endeavor. We take a walk, so to speak, in the realm of science, and we pursue whatever happens to present itself before our eyes by accident. Bacon compares scientific investigation with hunting; the observations that present themselves are the game. To continue the same comparison, one can add that if the game appears even when we are looking for it, it also happens that it appears when we are not looking for it or when we are looking for another kind of game. I will cite an example in which these two cases ocurred in succession. I will be careful at the same time to analyze every circumstance in this physiological investigation, in order to demonstrate the application of the principles which we developed in the first part of this introduction, principally in chapters I and II.

First example .-Rabbits were brought into my laboratory one day from the market. They were placed on a table where they urinated, and I happened to notice that their urine was clear and acid. This fact struck me, because normally rabbits, because they are herbivores, have cloudy and alkaline urine, while carnivores on the other hand, as is well known, have clear and acid urine. This observation of the acidity of the rabbits' urine made me think that these animals must have been in the nutritional condition of carnivores. I assumed that they had probably not eaten for a long time, and thus they found themselves transformed because of this starvation into true carnivorous animals living off their own blood. Nothing was easier than to verify this preconceived idea or hypothesis by experiment. I gave the rabbits grass to eat, and several hours later, their urine became cloudy and alkaline. These same rabbits were then starved, and after 24 or 36 hours at most their urine became clear and strongly acid again; and then it became alkaline again by giving them grass, etc. I repeated this very simple experiment a great number of times on the rabbits, and always with the same result. I then repeated it on a horse, an herbivorous animal which also has cloudy and alkaline urine. I found that, just as with rabbits, starvation produced a prompt acidification of the urine with a very considerable increase of urea, to the point that it sometimes crystallizes spontaneously in the cooled urine. The result of my experiments was that I thus arrived at this general proposition which was unknown at the time, that is, namely, all fasting animals feed on meat, such that herbivores have urine similar to that of carnivores.

Here we are dealing with a very simple, particular fact which allows us to follow easily the evolution of experimental reasoning. When we see a phenomena which we are not in the habit of seeing, we must always ask ourselves what it is related to, or to put it another way, what is its proximate cause; then a response or an idea arises in the mind which must be submitted to experiment. When I saw the acid urine of the rabbits, I instinctively asked myself what could be the cause. The experimental idea consisted of the spontaneous connection my mind made between the acidity of the rabbits' urine and the state of starvation which I considered as the true diet of flesh-eaters. The inductive reasoning which I implicitly made consisted of the following syllogism: the urine of carnivores is acid; now, the rabbits which I observed had acid urine; therefore they are carnivores, that is to say, in a state of fasting. This is what remained to be established by experiment.

To complete my experiment, I wanted in addition to see by means of autopsy if the digestion of meat in a rabbit was carried out in the same manner as in a carnivore. I found, in fact, all the phenomena of an excellent digestion in their intestinal reactions, and I established that all the chyliferous vessels were gorged with a very abundant, white and milky chyle just like in carnivores. But in connection with these autopsies, which offered a confirmation of my ideas on the digestion of meat in rabbits, a fact presented itself here which I had never considered and which became for me, as we shall see, the starting point for a new endeavour.

Second example (sequel to the preceding).-I happened to notice in sacrificing the rabbits which I had forced to eat meat, that the white and milky lymphatic vessels were first visible in the small intestine at the lower part of the duodenum, about 30 centimeters below the pylorus. This fact attracted my attention, because in dogs, the lymphatic vessels are first visible much higher in the duodenum and immediately below the pylorus. In examining the situation more closely, I noticed that this particularity in the rabbit coincided with the insertion of the pancreatic canal, which is situated in a very low point and precisely in the neighborhood where the lymphatic vessels begin to contain chyle made white and milky by the emulsion of fatty nutritive elements.

The fortuitous observation of this fact awakened in me an idea and generated in my mind the thought that the pancreatic juice could well be the cause of the emulsion of the fatty matter and consequently the cause of its absorption by the lymphatic vessels. Again I instinctively made the following syllogism: the white chyle is due to the emulsion of the fat; now, in rabbits, white chyle forms at the level where the pancreatic juice flows into the intestine; thus it is the pancreatic juice which emulsifies the fat and forms white chyle. This is what needed to be decided by experiment.

In view of this preconceived idea, I imagined and immediately carried out an experiment suitable for verifying the truth or falseness of my supposition. This experiment consisted of testing the properties of the pancreatic juice directly on neutral or alimentary fats. But pancreatic juice does not flow naturally outside of the body like saliva or urine, for example; its secreting organ is, on the contrary, deeply buried in the abdominal cavity. I was therefore forced to use the methods of experimentation in order to procure pancreatic fluid from a living animal in suitable physiological conditions and in a sufficient quantity. Only then could I carry out my experiment, that is to say, to control my preconceived idea, and the experiment proved that my idea was correct. In fact, pancreatic juice obtained in suitable conditions from dogs, rabbits, and many other kinds of animals, mixed with oil or melted fat, always emulsified instantaneously, and later acidified these fatty bodies in decomposing them, with the aid of a particular ferment, into fatty acids, cerin, etc., etc.

I will not elaborate on these experiments any further, since I have developed them at length in a specialized study [8] I have only wished to show how an initial observation made by accident on the acidity of rabbit urine gave me the idea to carry out experiments on their carnivorous nutrition, and how subsequently by following up on these experiments, I brought to light, without searching for it, another observation related to the special arrangement of the juncture of the pancreatic duct in rabbits. This unexpected second observation generated by the experiment, gave me in turn the idea to carry out experiments on the action of the pancreatic juice.

We see from the preceding examples how the observation of a fact or phenomenon, arriving unexpectedly by accident, engenders by anticipation a preconceived idea or hypothesis on the probable cause of the observed phenomenon; how the preconceived idea gives birth to reasoning which deduces the proper experiment to verify it; and how, in one case, it was necessary to have recourse to experimentation in order to work out that verification, that is to say, by using more or less complicated operative processes, etc. In the last example, experiment played a double role; it first judged and confirmed the predictions of the reasoning which had engendered it, but more so it provoked a new observation. One can thus call this kind of observation, an observation provoked or engendered by experiment. This proves that it is necessary, as we have said, to observe every result of an experiment, both those which are related to the preconceived idea and even those which have no relation to it. If we get into the habit of only seeing the facts related to our preconceived idea, we would often deprive ourselves of making discoveries; because it frequently happens that an unsuccessful experiment can provoke a very good observation, as the example which follows proves.

. . .

Fifth example .-Towards 1846, I wanted to make experiments on the cause of poisoning by carbon monoxide. I knew that this gas had been described as toxic, but I knew absolutely nothing about the mechanism of this poisoning; I therefore could not possess any preconceived opinion. What was to be done, then? I had to give birth to an idea by making a fact appear, that is to say, make an experiment to see. In fact, I poisoned a dog by forcing him to breathe carbon monoxide, and immediately after his death, I opened his body. I looked at the state of the organs and the fluids. What instantly attracted my attention was that the blood was crimson in all the vessels; in the veins as well as in the arteries, and in the right and left chambers of the heart. I repeated this experiment on rabbits, birds, and frogs; everywhere I found the same general crimson coloration of the blood. But I was distracted from following this investigation and I kept this observation for a long time without using it except to cite it in my courses in regards to the coloration of the blood.

In 1856, no one had investigated this experimental question further, and in my course at the College de France on toxic and medicinal substances , I took up again the study of carbon monoxide poisoning which I had begun in 1846. I found myself then in an ambiguous situation, because, at that time, I already knew that carbon monoxide poisoning renders the blood crimson throughout the entire circulatory system. It was necessary to make hypotheses and to establish a preconceived idea based on this first observation before proceeding further. Now, on reflecting on the fact of the reddening of the blood, I attempted to interpret it within the framework of all the preceding knowledge that I possessed on the cause of the color of the blood, and the following reflections presented themselves to my mind. The crimson color of the blood, I told myself, is peculiar to the arterial blood and is related to the presence of oxygen in great proportions, while the dark coloration is caused by the disappearance of oxygen and to the presence of a greater proportion of carbonic acid, so the idea came to me that the carbon monoxide, in preserving the crimson color in the venous blood, may have perhaps hindered the oxygen from changing into carbonic acid in the capillaries. However, it seemed difficult to understand how all this could be the cause of death. But still continuing my internal and preconceived reasoning, I added: if all of this were true, blood taken from the veins of animals poisoned by carbon monoxide should contain oxygen like arterial blood; that was what was necessary to see.

Following this reasoning founded on the interpretation of my observation, I carried out an experiment to verify my hypothesis relating to the persistence of oxygen in the venous blood. To do this, I passed a stream of hydrogen through the crimson venous blood taken from an animal poisoned by carbon monoxide, but I could not, as usual, displace the oxygen. I attempted the same on the arterial blood with no further success. My preconceived idea was therefore false. But this impossibility of obtaining oxygen from the blood of a dog poisoned by carbon monoxide provided a second observation for me which suggested new ideas according to which I formed a new hypothesis. What could have happened to the oxygen in the blood? It had not changed into carbonic acid, because I had not displaced any great quantity of this gas in forcing a current of hydrogen through the blood of the poisoned animal. Besides this supposition was in opposition to the color of the blood. I exhausted myself in conjecture concerning the manner in which the carbon monoxide could have made the oxygen disappear and, since gases displace one another, I naturally thought that the carbon monoxide could have displaced the oxygen and driven it from the blood. In order to confirm this, I resolved to change the experiment and to place the blood in artificial conditions which would permit me to recover the displaced oxygen. I then studied the action of carbon monoxide on the blood by artificial poisoning. To do this, I took a certain quantity of arterial blood from a healthy animal, and I placed this blood under mercury in a test tube containing carbon monoxide, and I consequently agitated the entire set up in order to poison the blood while protecting it from contact with the outside air. Then after a certain time, I looked to see if the air in the test tube, in contact with the poisoned blood, had been modified, and I determined that the air in contact with the blood was notably enriched with oxygen, at the same time that the proportion of carbon monoxide was diminished. It appeared to me after repeating these experiments under the same conditions that there had been a simple exchange volume for volume between the carbon monoxide and the oxygen in the blood. But the carbon monoxide in displacing the oxygen which it had driven from the blood, remained fixed in the blood corpuscles and could no longer be displaced by oxygen or by any other gas, such that death occurred by the death of the blood corpuscles, or to put it another way, by the cessation of the exercise of their physiological property which is essential to life.

This last example, which I have just related in a very succinct manner, is complete, and it shows from one end to the other how the experimental method proceeds and succeeds in coming to an understanding of the proximate cause of phenomena. First I knew absolutely nothing about the mechanism of the phenomenon of poisoning by carbon monoxide. I made an experiment to see, that is to say, for observation. I gathered a first observation on a special modification of the color of the blood. I interpreted that observation, and I made an hypothesis which experiment proved to be false, but this experiment furnished me with a second observation, upon which I reasoned anew using it as a starting point to make a new hypothesis on the mechanism of the removal of oxygen from the blood. In constructing these hypotheses successively on the facts as I observed them I finally arrived at demonstrating that carbon monoxide substitutes itself in the blood corpuscle in the place of oxygen, as a result of a combination with the substance of the blood corpuscle.

Here the experimental analysis has achieved its goal. It is one of the rare examples in physiology that I am happy to be able to cite. Here the proximate cause of the phenomenon of poisoning has been discovered and it is translated into a theoretical expression which takes into account all the facts and which includes at the same time all the observations and experiments. The theory thus formulated produces the principal fact from which all the others are deduced: carbon monoxide combines more strongly than oxygen with hemoglobin in a blood corpuscle. It has been proved quite recently that carbon monoxide forms a definite combination with hemoglobin, [12] such that the blood corpuscle, as if petrified by the stability of that combination, loses its vital properties. From then on, everything is deduced logically: carbon monoxide, because of its property of stronger combination, expels the oxygen from the blood which is essential for life; the blood corpuscles become inert and we watch the animal die with the symptoms of hemorrhage, from a true paralysis of the corpuscles.

But when a theory is good and offers the real and determined physico-chemical cause of phenomena, it not only covers the observed facts,but also can predict others and lead to reasoned applications, which will represent the logical consequences of the theory. Here we again encounter this criterion. In fact, if carbon monoxide has the property of removing oxygen by combining with the blood corpuscle in its place, one could use this gas to analyze the gases in the blood and in particular to determine the existence of oxygen. I deduced this application from my experiments, which today has generally been adopted today. [13] Applications to legal medicine have also been made of this principle of carbon monoxide for uncovering the coloring matter of blood, and from the physiological facts pointed out above we can also already derive consequences relating to hygiene, to experimental pathology, and notably to the mechanisms of certain kinds of anemia.

Without doubt, in all the deductions from the theory, experimental verification will always be necessary as usual, and logic is not sufficient; but that is because the conditions of the action of carbon monoxide on the blood can present other complex circumstances and a host of details that the theory cannot yet predict. Otherwise, as we have often said (Cf. p. 52), we could reach conclusions only through logic, and without the need of experimental verification. It is thus because of new and unforeseen variables, which can introduce themselves into the conditions of a phenomenon, that logic alone is never sufficient in the experimental sciences. Even when we have a theory which appears good, it is only relatively good and it always encompasses a certain proportion of the unknown.

We have already said (p. 46) and we shall see later that in noting an observation, we must never go beyond the facts. But it is not the same in carrying out an experiment. I want to demonstrate therefore that hypotheses are indispensable and that their utility lies precisely in leading us outside of the fact and carrying science forward. Hypotheses have as their object to make us not only carry out new experiments, but also often discover new facts which we would not have noticed without them. In the preceding examples, we have seen that one can begin from a particular fact to gradually rise towards more general ideas, that is to say, towards a theory. But it also happens, as we have just seen, that one can begin from an hypothesis deduced from a theory. In this case, although it concerns a reasoning logically deduced from a theory, it is nevertheless still an hypothesis that we must verify by experiment. Here in fact the theories only represent to us an assemblage of previous facts on which the hypothesis is supported, but cannot be used to demonstrate it experimentally. We have said that in this case we must not submit to the yoke of theory, and that the best condition for finding truth and for making progress in science was to retain the independence of the mind (Cf. p. 80). The following examples will prove this.

First example .-In 1843, in one of my first works, I undertook a study to determine what happened to different alimentary substances during nutrition. I began, as I have already said, with sugar, a definite substance which is easier to recognize and to follow throughout the economy of an organism than any other substance. To this end, I injected solutions of cane sugar into the blood of some animals and I established that this sugar, even when injected into the blood in small doses, passed into the urine. I later recognized that the gastric juice in modifying or transforming this cane sugar, rendered it assimilable, that is to say, destructible in the blood. [14]

Then I wanted to know in which organ this alimentary sugar disappeared and I hypothesized that the sugar which nutrition introduced into the blood might be destroyed in either the lungs or the general capillaries. In fact, the dominant theory at that time, which naturally was my starting point, claimed that the sugar which existed in animals originated exclusively in food and that it was destroyed in the animal organism by the phenomenon of combustion, that is to say, respiration. This is why sugar was given the name respiratory nutriment. But I was immediately led to see that the theory of the origin of sugar in animals, which served as my starting point, was false. In fact, by a succession of experiments which I will describe later, I did not find the organ which destroyed sugar, but on the contrary I discovered an organ which created that substance, and I also found that the blood of all animals contained sugar, even when they did not consume it. I therefore established a new fact, unexpected from the theory and which no one had ever noticed, undoubtedly, because they were enthralled by contrary theoretical ideas which they had accepted with too much confidence. I then abandoned right away all my hypotheses on the destruction of sugar, to follow up on this unexpected result which has since become the fertile origin of a new path of investigations as well as a mine of discoveries which is still far from being exhausted.

In these investigations I proceeded according to the principles of the experimental method which we have established; that is to say, in the presence of a new well-established fact in contradiction to a theory, instead of preserving the theory and abandoning the fact, I kept the fact which I had studied, and hastened to drop the theory, in conformance with that principle which we discussed in the second chapter: When a fact which we encounter is in opposition to a prevailing theory, we must accept the fact and abandon the theory, even when that theory, upheld by great names, has been generally adopted.

We must distinguish, as we have said, between principles and theories and never to believe in theories in an absolute manner. Here we had a theory according to which it was believed that only the vegetable kingdom possessed the power to create the primary substances which the animal kingdom was supposed to break down. According to this established theory upheld by the most illustrious contemporary chemists, animals were incapable of producing sugar in their organism. If I had believed in that theory absolutely, I would have had to conclude that my experiment must have been contaminated with error, and perhaps experimenters less distrustful than myself would have immediately condemned my experiment and would have not lingered for long over an observation which could be the source of error according to the theory, since the observation showed sugar in the blood of animals subjected to a diet lacking starchy or sugary materials. But instead of preoccupying myself with the validity of the theory, I only concentrated on the fact and attempted to establish its reality. Thus through new experiments and by the method of suitable counter-proofs, I was led to confirm my original observation and to discover that the liver was an organ where in certain given situations animal sugar is formed which consequently flows throughout the bloodstream and throughout the tissues and organic fluids.

This animal glycogenesis, that is to say the faculty possessed by both animals and plants to produce sugar, is now an established fact in science, although we have not yet determined a plausible theory to account for the phenomenon. The new facts which I have brought to light, have been the source of a great number of studies and many diverse theories in apparent contradiction among themselves as well as with my own. When we enter into new ground, we should not be afraid to express even risky views in order to excite investigations in all directions. We should not, following the expression of Priestly, remain inactive through false modesty or the fear of being mistaken. I therefore advanced some more or less hypothetical theories on glycogenesis: since mine were offered, others have been made: my theories, just as those of others, will only live as necessarily partial and provisional theories must live, when a new series of investigations begins; they will soon be replaced by others which represent a more advanced state of science, and so forth. Theories represent successive degrees by which science ascends in enlarging its horizon more and more, because the further they are advanced, the more facts theories encompass and explain. True progress consists of exchanging our theory for new ones which go further than the original, until we find one that rests on a greater number of facts. In the case we are discussing, the point is not to condemn the older theory to the profit of the newer. What is important is to open a new road, because what will never perish are well observed facts which ephemeral theories have brought to life; these are the only materials upon which the edifice of science will be built on the day when she possesses a sufficient number of facts and when she has penetrated far into the analysis of phenomena to discover the law or the exact causation.

In summation, theories are only hypotheses verified by a lesser or greater number of facts; those which are verified by the greatest number of facts are the best; but still they are never definitive and one should never believe in them absolutely. We have seen from the preceding examples, that if we had placed our entire confidence in the prevailing theory of the destruction of sugar in animals, and if we had only sought its confirmation, we would not have followed up on the new facts which we encountered. The hypothesis founded on a theory provoked the experiment, but as soon as the results of the experiment appeared, the theory and the hypothesis had to disappear, because the experimental fact was no more than an observation made without any preconceived idea (Cf. p. 40).

Second example, sequel to the last.-After having discovered, as I have mentioned above, that animal liver contains sugar in its normal state and with every kind of diet, I wanted to know the proportion of this substance and its variations in certain physiological and pathological states. I thus began determining the amount of sugar in the livers of animals placed in various defined physiological conditions. I always made two simultaneous determinations of the sugary material in the same liver tissue. But one day pressed for time, it happened that I was not able to make my two analyses at the same time; I immediately made a rapid determination after the death of the animal, and left the other for the next day. But I found this time much greater quantities of sugar than those which I had obtained the previous day in the same hepatic tissue, and I noticed in addition that the proportion of sugar which I had found in the liver, immediately examined after the death of the animal, was much lower than what I had encountered in other experiments which I had made known as giving the normal proportion of hepatic sugar. I did not know to what to attribute the peculiar variation obtained from the same liver and with the same analytical method. What was to be done? Should I have considered the two discordant amounts as the result of an unsuccessful experiment and to ignore them? Should I have averaged the results of these two experiments? That is an expedient which many experimenters would have chosen to deliver themselves from this awkward situation. But I do not approve of this manner of operating for reasons which I have given elsewhere. I have said in effect that nothing must be overlooked in the observation of facts, and I regard it as an indispensable rule of experimental criticism (p. 299) to never admit without proof the existence of a cause of error in an experiment, and to always search for a reason for all the abnormal circumstances which we observe. Nothing occurs by accident, and that which seems accidental is nothing more than an unknown fact which could become, if it were explained, the occasion of a more or less important discovery. This is what happened to me in this case.

I wanted to know in fact what the reason was for the two very different amounts of sugar in the liver of my rabbit. After convincing myself that there was no error in the method of measuring the sugar; and after establishing that the different parts of the liver are equally rich in sugar, the only thing left to examine was the influence of time which had elapsed since the death of the animal, up until the time of my second measurement. Up until then, I had always made my experiments, without attaching any importance to the fact, several hours after the death of the animal, and for the first time, I found myself in the situation of immediately taking a measurement several minutes after the death of the animal, and leaving the other until the next day, that is to say 24 hours afterwards. In physiology, questions of time always have great importance, because the organic matter undergoes numerous and incessant changes. Thus some chemical modification could have been produced in the hepatic tissue. To reassure myself, I made a series of new experiments which dissipated all the obscurities by showing me that the liver tissue constantly enriches itself with sugar during a certain time after death, such that one can find very variable quantities of sugar, based on the moment in which one makes the examination. I was thus led to rectify my former measurements and to discover this new fact; namely, that considerable quantities of sugar are produced in the livers of animals after death. I demonstrated, for example, by passing a stream of cold water injected by force through the hepatic vessels into a still warm animal liver soon after death, that one can completely remove the sugar contained in the hepatic tissue; but the next day, or several hours afterward, when I brought the liver to a mild temperature, I found the liver charged again with a great quantity of sugar produced since the washing. [15]

This second series of facts is today widely accepted in science and has contributed to great progress in the understanding of glycogenesis in animals. I have just succinctly described how these facts were discovered and how their starting point proceeded from an apparently useless experimental circumstance. I have described these events in order to prove that we should never neglect anything in experimental investigations; because all accidents have their necessary cause. We should never become too absorbed therefore by the thought one is following, nor fool ourselves about the value of our scientific ideas; we must always keep our eyes open to every event, and maintain a doubting and independent mind (p. 138) disposed to examine everything that happens and not to let anything pass without searching for the reason why. We must remain, in a word, in an intellectual disposition which seems paradoxical, but which, in my opinion, represents the true mind of the investigator. We must have a robust faith and not believe; I explain this by saying that we must believe firmly in principles and to doubt formulas; that we must remain unshakable with respect to the principles of experimental medicine (determinism) and not to believe absolutely in theories. The aphorism which I have just expressed can be supported by what we have developed elsewhere (Cf. p. 116), namely, that the principles of the experimental sciences are in our mind, while formulas exist in exterior things. In practice we are forced to believe that the truth (or the provisional truth, at least) is represented by the theory or by the formula, but in scientific philosophy those who place their faith in formulas or theories are wrong. All human knowledge is directed towards finding the correct formula or the correct theory of truth in some realm. We always approach truth, but will we ever completely find it? This is not the place to develop these philosophical ideas; let us return to our subject and look at a new experimental example.

Third example .-Around 1852, I was led by my studies to make experiments on the influence of the nervous system on the phenomena of nutrition and heat. It had been observed before me that in a great many cases, complex paralyses situated in the mixed nerves are followed at one time by a heating, and another time by a cooling of the paralyzed parts. Now here is how I reasoned to explain the fact by relying on observations, on one hand, and on the other hand, on the prevailing theories relative to the phenomena of nutrition and heat. The paralysis of the nerves, I told myself, must lead to the cooling of the nerves by slowing down the phenomena of combustion in the blood, since these phenomena are considered the cause of animal heat. Now, on the other hand, anatomists have noticed for a long time that the sympathetic nerves in particular accompany the arteries. Thus, I thought by induction, it must be the sympathetic nerves which, in the lesion of a mixed trunk of nerves, act to slow down the chemical phenomena in the capillary vessels, and it is their paralysis which must bring about the cooling of the parts. If my hypothesis were true, I added, it should be verifiable by cutting only the sympathetic vascular nerves leading to a certain part and carefully leaving the other nerves. I should then obtain a cooling by paralysis of the vascular nerves without the movement or sensibility disappearing, since I would have left the motor and ordinary sensory nerves intact. In order to carry out my experiment I sought a suitable method of experimentation which would allow me to cut the vascular nerves alone while leaving the other nerves. Here the choice of animal became important relative to the solution of the question (p. 213); but the anatomical arrangement which isolates the great cervical sympathetic nerve in certain animals such as the rabbit and the horse, made this solution possible.

According to this reasoning, I therefore cut the great sympathetic nerve in the neck of a rabbit to control my hypothesis and to see what would happen to the change in heat in the side of the head where that nerve was branched out. I had been led, as we have just seen, by a reliance on the prevailing theory and by previous observations, to make the hypothesis that the temperature should be lowered by the cutting of the sympathetic nerve. Now precisely the opposite happened. Soon after severing the great sympathetic nerve in the middle of the neck of the rabbit, I noticed in the entire corresponding side of the head a considerable increase in activity in the circulation accompanied by a rise in heat. The result was therefore exactly opposite to what my hypothesis deduced from the theory had made me predict; but I proceeded as usual, that is to say I abandoned immediately the theories and the hypotheses in order to observe and study the fact in itself in order to determine as exactly as possible the experimental conditions. Today these experiments on the vascular and thermo-regulatory nerves have opened up a new road of research and have become the subject of a great number of works which, I hope, will one day furnish results of great importance to physiology and pathology. [16]

This example proves, like the preceding, that in experiments one can encounter results different from those which we expect from the theories and hypotheses. But if I am calling particular attention to this third example, it is because it offers us an important lesson, that is, without this directing hypothesis of the mind, the experimental fact which contradicted it would never have been noticed. In fact, I was not the first experimenter who had cut the cervical portion of the great sympathetic nerve in living animals. Pourfour du Petit carried out this experiment at the beginning of the last century and he discovered the effects of this nerve on the pupil by reference to an anatomical hypothesis according to which this nerve was supposed to carry the animal spirits into the eyes. [17] Since then many physiologists have repeated the same operation in order to verify or to explain the modifications of the eye which Pourfour du Petit was the first to notice. But none of these physiologists had noticed the phenomenon of the rise in temperature of the parts which I am speaking of and never linked it to the severing of the great sympathetic nerve, even though this phenomenon must have necessarily been produced under the eyes of everyone who, before me, had cut that part of the sympathetic nerve. The hypothesis, as we see, had prepared my mind to see these things from a certain point of view provided by the hypothesis itself, and what that proves is that even I, like the other experimenters, had often cut the great sympathetic nerve to repeat the experiment of Pourfour du Petit, without seeing the fact of heating which I discovered later when an hypothesis led me to make investigations in this direction. The influence of the hypothesis is thus very evident here; we had the fact under our eyes and we did not see anything because it said nothing to the mind. It was extremely simple to observe however, and ever since I pointed it out, every physiologist without exception has noticed and verified it with the greatest facility.

What general conclusion can the physiologist draw from the preceding examples? He must conclude that in the present state of biological science the ideas and the theories which prevail only represent very circumscribed and precarious truths which are destined to perish. He should consequently hold little confidence in the real value of these theories, but use them as intellectual instruments necessary to the evolution of the science and appropriate for stimulating the discovery of new facts. Today the art of discovering new phenomena and establishing them exactly must be the special object of all biologists. We must at the same time ground experimental criticism by creating rigorous methods of investigation and experimentation which will permit us to establish observations in an indisputable manner and consequently to banish errors of facts which are the source of unsuccessful theories. Any one who attempted now to support a generalization for the entire field of biology would demonstrate that he had no exact idea of the present state of that science. Today the problem of biology has hardly been posed, and even as it necessary to assemble and cut the stones before we dream about constructing a building, so it is also necessary first to assemble and prepare the facts which must constitute the science of living bodies. This role falls to experimentation-its method is fixed-but the phenomena which it must examine are so complex that the real mover of the science for the moment will be the person who provides several principles of simplification in analytical methods or who perfects the instruments of research. When enough clearly established facts exist, generalizations never slow us down. I am convinced that in the evolving experimental sciences, and particularly in those which are as complex as biology, the discovery of a new instrument for observation or experimentation renders greater theoretical service than all the theoretical and philosophical dissertations. In fact, a new process, a new method of investigation increases our power and allows the possibility of discoveries and investigations which would have been impossible without them. Thus investigations into the formation of sugar in animals could not be carried out before chemistry had given us reagents to recognize sugar which were more sensitive than those we had before.

NOTES

[1] Bacon, Works, edition of Fr. Riaux, Introduction, p. 20.

[2] J. de Maistre, Examen de la philosophie de Bacon.

[2] De Remusat, Bacon, sa vie, son temps et sa philosophie, 1857.

[4] Descartes, Discours sur la methode.

[5] ["Corps bruts." Editor.]

[6] Letter to J.C. Mertrud, p. 5. Year VIII.

[7] Claude Bernard, Leçons sur la physiologie et la pathologie du systeme nerveux. Leçon d'ouverture, December 17, 1856. Paris, 1858, t. 1-Cours de pathologie expérimentale, The Medical Times , 1860.

[8] Claude Bernard, Mémoire sur le pancréas et sur le rôle du suc pancréatique dans les phénomènes digestifs. Paris, 1856.

[9] Claude Bernard, Leçons sur les propriétés physiologiques et les altérations pathologiques des liquides de I'organisme. Paris, 1859, VOL 2.

[10] Claude Bernard, Sur la quantite d'oxygène que contient le sang veineux des organes glandulaires (Compt. rend. de l'Acad. des sciences, vol. 47, September 6, 1858).

[11] Cf. Claude Bernard, Leçons sur les effets des substances toxiques. Paris, 1857; Du curare (Revue des deux mondes , September 1, 1864).

[12] Hoppe-Seyler, Handbuch der physiologisch and pathologisch chemischen Analyse. Berlin, 1865.

[12] Claude Bernard, De l'emploi de l'oxyde de carbone pour la détermination de l'oxygène au sang ( Compt. rend. de l'Acad. des sciences , meeting of September 6, 1858, vol. 47).

[14] Claude Bernard, doctoral thesis in medicine. Paris, 1842.

[15] Claude Bernard, Sur le mécanisme de la formation du sucre dans le foie (Comptes rendus de l'Acad. des sciences, September 24, 1855).-Sequel (Comptes rend. de l'Acad. des sciences, March 22, 1850

[16] Claude Bernard, Recherches expérimentales sur le grand sympathique, etc. (Mémoires de la Société de biologie, vol. 5, 1853 ).-Sur les nerfs vasculaires et calorifiques du grand sympathique (Comptes rendus de I'Acad. des sciences, 1852, vol. 34, 1862, vol. 55).

[17] Pourfour du Petit, Mémoire dans lequel il est démontré que les nerfs intercostaux fournissent des rameaux qui portent des esprits dans les yeux (Historie de I'Académie pour l'année 1727).