CHAPTER III

.

On the Origin of Ferments properly so called.

The new process of brewing, which it is the principal object of this work to explain, and which will follow as an immediate and inevitable deduction from the novel facts herein demonstrated, cannot be fully understood without a knowledge of all the principles upon which it is founded. One of the most essential of these has reference to the purity of our fermentation. We should gain but little from the use of a yeast uncontaminated by any foreign germs if natural organic substances had the power of organizing themselves by means of spontaneous generation, or by some transformation which took place amongst them, or even by a conversion of certain microscopic beings into certain others. Theories of this kind are still warmly advocated, but, to our thinking, rather from sentimental considerations or prejudice than from any basis of serious experimental proofs.

Be this as it may, we must free our minds from all suppositions which might qualify the exactness of the principles upon which our new process is founded, or cause any doubt in the minds of our readers as to the possibility of its application and the benefits to be derived from its adoption.

§ I.—On the Conditions which cause Variations in the Nature of the Organized Products existing in Infusions.

We have proved by experiment, in the preceding chapter, that a few minutes’ boiling renders liquids, and more especially wort, absolutely free from liability to change when in contact with pure air, that is, air which contains none of the germs of organisms that are continually floating about in the atmosphere.

What is true in the case of wort is equally so in the case of all organic liquids; there is not a single one that could not be rendered inaccessible to any subsequent change if it were brought, first of all, to a suitable temperature, which would vary with the nature of the liquids. Amongst them there are some which, like vinegar, lose their tendency to change after having been rapidly raised to a temperature of not more than 50° C. (122° F.); others, like wine, require a greater heat. Wort, to which no hops have been added, should be subjected to a temperature of not more than 90° C. (194° F.); milk to about 110° C. (230° F.).[21]

It is easy to show that these differences in temperature, which are required to secure organic liquids from ultimate change, depend exclusively upon the state of the liquids, their nature, and, above all, on the conditions that affect their neutrality, whether towards acidity or alkalinity; for it is not difficult to observe that the least changes in these respects lead to considerable variations in the temperatures which we must employ.[22] We could adduce many examples of this. The only difference between the nature of must and that of wine is caused by fermentation. We may say the same thing of wort and beer, and, better still, of new milk and sour milk. Must, to be secured from change, requires a much higher temperature than wine does; similarly, wort requires a much higher temperature than beer. Milk must be heated to about 110° C. (230° F.), as we have just stated, but sour milk would require 20° C. or 30° C. (36° F. or 54° F.) less. Wine, when fresh, ceases to be liable to change after it has been brought to a temperature below 100° C. (212° F.); it requires a temperature of more than 100° C. in the presence of carbonate of lime.

As regards the explanation of the influence which acidity or alkalinity exerts in diminishing or increasing the temperature required to protect infusions and organic matters from ultimate change, although this is a subject which claims special study, we are inclined to believe that acidity permits, and alkalinity prevents, the penetration of moisture into the interior of the cells of the germs belonging to infusions, so that in heating the outer cases of these cells in an alkaline medium we heat the germs in a dry state; and in heating the outer cases in an acid medium we heat the germs when they are moist. We all know that these conditions make a great difference in the resistance which bodies offer to the action of heat. A particle of mould which, in a moist state, cannot survive a temperature of from 60° C. to 100° C. (140° to 212° F.), will preserve its fecundity even if heated to 120° C. (248° F.), if it has been previously well dried.[23]

The nature of the spontaneous productions which we see appear in organic liquids is affected to a remarkable extent by the smallest change in the compositions of those liquids. Generally speaking, as we have often proved in our former works, a feeble acidity is unfavourable to the development of bacteria and infusoria, and, on the other hand, favourable to the growth of mould. A liquid which is neutral or of feeble alkalinity behaves in an exactly inverse manner.

Those who support the theory of spontaneous generation seek to find in the natural differences between the organic productions of various liquids which are simultaneously exposed to the same atmosphere, an argument in favour of their doctrine. These differences, however, are only an effect of the greater or less fitness of a peculiar liquid for a certain kind of growth. When an acid organic liquid, such as the must of grapes for example, is exposed freely to the air, it is besieged simultaneously by spores of _mucedines_, as well as germs of _bacteria_, _leptothrix_, _vibrios_, _&c._, but the latter germs are checked in their development, if, indeed, they are not actually destroyed, by the acidity of the liquid; and we should never find them there in their adult state.

Most moulds, on the other hand, thrive in acid liquids, and therefore they are generally found alone. If we began by saturating must with carbonate of lime, previously dried or otherwise, we should observe opposite phenomena; bacteria, lactic ferments and butyric vibrios would invade our fields long before the spores of mould had time to grow, since the germination of these proceeds very languidly in neutral or alkaline liquids, and an infusion once occupied by a living organism has much trouble in nourishing others; the early developments consume the alimentary substances, especially the oxygen.

Differences as marked as these in the adaptability of certain liquids to certain growths give rise to innumerable illusions, and are one of the chief sources of error in the study of this subject. If we sow in an acid liquid, such as must, an alcoholic ferment, the development of which is not arrested by the acid character of our medium, it will multiply there, and we shall have no difficulty in growing it over and over again in the same acid medium. This being the case, let us suppose that our alcoholic ferment is impure—let us say, mixed with filaments of turned wine, which are due to a ferment checked in its development by the peculiar qualities of the must. In repeating the growth of this alcoholic ferment in the must the filaments which were, by supposition, present in our first sowing, and which cannot reproduce themselves in the must, or do so with great difficulty, will become very scarce in the fields of our microscope; they will not, however, cease to exist, for the repetition of our attempts to grow them only serves to spread the original germs over a larger surface; and, although the eye fails to detect them, they will only have become more difficult to discover. At this point the experimentalist is in danger of falling into error, for when he no longer perceives the foreign ferment he will be inclined to believe that it has vanished, and that he may regard the alcoholic ferment as being free from all impurity, without testing for the purity by a direct experiment.

An example of this mistake is to be found in a recent work by M. Jules Duval. This writer has published a theory according to which yeast becomes transformed into lactic ferment, and likewise into other ferments—that of urea, for example—the only condition of change, according to M. Jules Duval, being that we should cultivate it in suitable mediums. The proofs by which he supports his conclusion are altogether inadmissible, and a simple glance at his experiments enables us to detect innumerable causes of error. M. Duval believes that yeast becomes transformed into lactic ferment from the fact that he obtained a fermentation which furnished lactate of lime and lactic ferment from some sour milk to which he had added some glucose, chalk, and phosphate of ammonia before impregnating it with yeast; but he took no steps to secure himself against introducing into his medium—which was, as a matter of fact, well adapted to lactic fermentation, inasmuch as it was a little alkaline—an alcoholic ferment containing impurities. This was the crucial point in his experiments. M. Duval recognizes this, but he deceives himself when he says, without proof:—“My alcoholic ferment is pure, for I have grown it over and over again in must, preserved in flasks prepared after the manner of those which M. Pasteur uses in his experiments.” Here we have merely a simple assertion; a direct experimental test might have proved that the yeast was impure.

Yeast cannot transform itself into lactic ferment. No matter what the medium may be in which it is sown, _if it is actually pure_ it will never present the least trace of lactic ferment or of any other ferments. By certain changes in the nature of the medium, the temperature, and other conditions, the cells of the ferment may become oval, elongated, spherical, and larger or smaller in size, but they will never produce the most minute quantity of lactic ferment or lactic acid. The whole theory of the transmutation of ferments, which M. Duval has published, is imaginary.[24]

We have asserted that the source from which we obtain our supply of the substances that we expose to contact with the air may likewise furnish a reason for the development of vegetable or animal organisms which make their appearance in our infusions. This may be easily understood. If we expose the infusions to temperatures more or less high, with the object of destroying the vitality of the germs which they may contain, we completely suppress all germs originating from two different sources—those which the infusions may have acquired directly from the atmospheric air, or from the dust upon our utensils, and those which may have been introduced by the materials used in manufacturing our infusions or decoctions, which materials must have been brought from some distance. An infusion, after having been heated to a sufficient degree, can harbour and nourish only such germs as are conveyed to it by the air after the heating. These floating germs are far from being as varied in their nature as it pleases those to believe who are tied down by their arbitrary and faulty interpretation of the knowledge that we have acquired, and the discussions in which we have taken part, during the last fifteen years. Air, unless in violent agitation, can hold only the most minute particles in suspension. The observations which have been recorded concerning organisms of spontaneous growth found in infusions, have always been made in sheltered places—in rooms or laboratories, the atmosphere of which is, relatively speaking, very still. For this reason, in liquids that have been subjected to heat, the _flora_ and _fauna_—if we may use such an expression—are very poor, and all the more so because, as we have recently had occasion to remark, a great number of the organisms which would spring into existence of their own accord, if they were allowed sufficient time for germination, are kept back by others of a more rapid development. The truth of this is evident from the fact that we may observe greater variations in the nature and number of species of living organisms, if we divide one infusion amongst several vessels which are immediately closed up again, than if we leave our infusion in contact with an unlimited volume of surrounding air. By this means we expose each portion of the liquid to no other germs than those existing in a state of suspension in the volume of air introduced into the vessels; and it so frequently happens that we obtain a variety of germs which, coming into contact with a liquid adapted to their nutrition, without having mixed with others, finally multiply there, in consequence of no other organisms of greater

## activity occurring to impede their slow and laborious propagation.

The nature of the products resulting from raw infusions—that is, those obtained, without heating, from the maceration of organic substances, such as leaves, fruits, grains, or the organs of plants or animals—is much more varied. The reason of this is that such substances generally carry with them not only the particles of dust existing in air that is in motion, but also microscopic parasites, which find a congenial resting-place on their surface or its vicinity. We may cite a few accurate observations on this point, for the subject is one of great interest.

If we boil an infusion of hay, and then expose it to contact with the air in a room, all its productions will be derived from such germs as a comparatively still air can carry about; thus, we shall very rarely find any _colpoda_ in our infusion, for the germs of these infusoria, consisting of rather large cells, can scarcely exist in a state of suspension in motionless air, in spite of their extraordinary diffusion in nature. On the other hand, we almost invariably find _colpoda_ in macerations of raw hay. This difference is easily accounted for; the

## particles of dust adhering to the surface of hay, especially that which

comes from marshy districts, contain the germ-cells of _colpoda_ in abundance. The reason is obvious; rain falls on a meadow and forms little pools of water about the roots of the herbs that grow there; this water remains for some time, and very soon swarms with a multitude of infusoria, especially _colpoda_. Dryness follows; the _colpoda_ becomes encysted, and forms a dust that is wafted by the winds on to the blades of grass, so that the mower will carry away not only his hay, but also myriads of _colpoda_, as well as spores of _mucedines_ and other organisms.[25]

The maceration of pepper will give us some infusoria hardly ever found in other infusions, the reason of this being that such infusoria exist where the pepper grows—in other words, their germs are exotic. That the infusion of a special plant should give us special infusoria, is scarcely more surprising than the discovery of a particular parasite or insect existing on a particular plant, and not on others of a different species that grow near it. Thus it happens that the ferment-germs of must exist on the surface of grapes, whether detached or in clusters. It is only natural that we should find the organ or the plant that is destined later on to become the food of a parasite serving as a habitation for the germs of that parasite.

§ II.—Experiments on Blood and Urine taken in their Normal State, and Exposed to Contact with Air that has been Deprived of the Particles of Dust which it Generally holds in Suspension.

Recourse to the application of heat, in the first place, is an excellent means, as we have just seen, of procuring organic liquids free from all disturbing germs; but there is a still more remarkable and instructive, we may even say more unlooked for, method of securing this result, which may be described as in some measure borrowed from the nature of things. It consists in seeking purity in the natural liquids of animals and plants. It is difficult to understand how the liquids circulating in the organs of animal bodies, such as blood, urine, milk, amniotic fluid, and so on, can possibly secrete the germs of microscopic organisms. There would be excellent opportunities for these germs to propagate themselves if they actually did exist in the liquids appertaining to the animal economy. Life in all probability would become impossible in the presence of such guests. A proof of this is to be found in the multitude of diseases which many of the greatest minds of modern times attribute to parasitic developments of this nature. Medical men of high authority agree in thinking that the questions of contagion and infection will find solutions from the obscurity in which they are now involved in a careful study of ferments, and that hygienists and physicians should labour to secure by every possible means the destruction of the germs of ferments, and should strive to check _their_ development, and prevent the evils which _they_ cause when developed. Great progress has already been made in this direction, and we deem it a signal honour that our researches on the subject have been considered, even by those by whom this progress has been accomplished, as the source from which they derived their first inspirations. We shall, doubtless, be excused by our readers if we recall this fact in relating certain historical details which are especially necessary in order that they may comprehend the principles that we are endeavouring to explain in these “studies.”

It is a matter of regret to us, however, that the facts which we have established should have been accredited with any importance beyond that which is their due. The exaggeration of novel ideas invariably leads to a reaction, which, again, overshooting the mark, brings into disrepute even those points in which such ideas are perfectly just, or, at all events, worthy of serious consideration. There are certain symptoms of such a reaction in the case of our theories: they are evident in the tendency of unreflecting minds to give a total denial to the fact that certain diseases may be derived from certain ferments—organized and living ferments—of the nature of those which have been discovered in the course of the last twenty years. We should be guided by facts, whichever side of the question we espouse, and by facts alone we should test the truth of doubtful discoveries. We are but on the threshold of the exploration of our subject, and we should strive to discover new facts in connection with it, and should deduce from these, whatever they may be, only such conclusions as they may strictly warrant. Unfortunately, there is amongst physicians a tendency to generalize by anticipation. Many of them are men of rare natural or acquired talent, endowed with keen powers of intellect, and the art of expressing themselves fluently and persuasively; but the more eminent they are, the more they are occupied by the duties of their profession, and the less leisure they have for the work of investigation. Urged on by that thirst for knowledge which belongs to superior minds, and perhaps, in some measure, through associating with the upper classes of society, which are becoming more and more interested in science, they eagerly seize upon easy and plausible theories, readily adapted for statement which is general and vague just in proportion to the unsoundness of the facts on which they are based. When we see beer and wine undergo radical changes, in consequence of the harbour which those liquids afford to microscopic organisms that introduce themselves invisibly and unsought into it, and swarm subsequently therein, how can we help imagining that similar changes may and do take place in the case of man and animals? Should we, however, be disposed to think that such a thing must hold true, because it seems both probable and possible, we must, before asserting our belief, recall to mind the epigraph of this work: _the greatest aberration of the mind is to believe a thing to be, because we desire it_.

One of the most distinguished members of the Academy of Medicine, M. Davainne, who was the first to give his attention to rigorous experiments on the influence that organic ferments exercise on the production and propagation of infectious diseases, declares that the idea of his researches on _splenic fever_ and _malignant pustule_ was suggested to him by his perusal of our work on butyric fermentation, published in 1861. In 1850 this gentleman and M. Rayer discovered in the blood of animals attacked by these diseases minute filiform bodies, to which they paid little attention, and which M. Davainne recollected, when he came across our Memoir. He had the foresight to conjecture—a conjecture that was soon confirmed most decisively by his researches—that the former disease, known under the name of _sang de rate_, might be the production of a fermentation analogous to the butyric, in which the minute filiform bodies observed by Rayer and himself, in 1850, played the part which vibrios fill in butyric fermentation. Within two years of this the first works of Messrs. Coze and Feltz appeared. These clever and courageous experimentalists avowed that their beautiful researches had been suggested to them by the perusal of my work on putrefaction, published in 1863. We might also quote the striking and admirably conceived experiments of Dr. Chauveau, on castration.[26] We cannot, however, refrain from reproducing here a letter addressed to us in 1874 by the celebrated Edinburgh surgeon, Mr. Lister:—

“Edinburgh, Feb. 10, 1874.

“DEAR SIR,—Will you permit me to beg your acceptance of a pamphlet which I forward to you by this post, and which describes certain inquiries into a subject upon which you have thrown so much light—the theory of germs and fermentation? It gives me pleasure to think that you will peruse with some interest what I have written about an organism that you were the first to study in your Memoir on lactic fermentation. I do not know if you ever see the records of British surgery. If you have perused them you may have observed from time to time notices of the antiseptic system which I have been endeavouring for the last nine years to bring to perfection. Permit me to take this opportunity of offering you my most hearty thanks for having demonstrated by your brilliant researches the truth of the theory of putrefactive germs, and for having afforded me in this manner the sole means of perfecting the antiseptic system.

“Should you ever come to Edinburgh I am sure that you will be truly gratified to see in our hospital the extent to which the human race has profited by your work. I need hardly add, that I should have great satisfaction in showing you how greatly surgery is indebted to you.

“Excuse the freedom which I have taken in addressing you, on the grounds of our common love for science, and believe in the profound esteem of yours, very sincerely, JOSEPH LISTER.”

The wad dressing of Dr. Alphonse Guérin, surgeon at the Hôtel-Dieu, Paris, which has already rendered great assistance to surgery, and has been the subject of a very favourable report at the Academy of Sciences in Paris, was invented by its author in consequence of certain reflections suggested to him by the perusal of our researches. The commission which framed the report made, through M. Gosselin, some wise reservations in the case of certain theoretical ideas which M. Guérin had not sufficiently proved by experiment. We have no doubt, however, that when the matter is thoroughly examined, facts will confirm the truth of the wide views entertained by the surgeon of the Hôtel-Dieu.

Dr. Déclat has founded quite a new system for the treatment of infectious diseases, which is based upon the use of one of the best known antiseptics, phenic acid. His theory, which he affirms was suggested to him by our studies on fermentations, is, that the diseases which transmit themselves are, each of them, the product of a special ferment, and that both medical and surgical professors of therapeutics should make it their study to prevent exterior ferments from penetrating into the liquids of our economy, or in the event of these ferments having found their way into the system, to discover _antiferments_ for their destruction, without effecting any change in the vitality of the histological elements of the liquid or tissues.

There is no doubt that extreme caution must be exercised in dealing with questions of this kind, as M. Sédillot has authoritatively remarked; but at the same time it cannot be denied that the more such questions are discussed with exactness, the more those celebrated practitioners who originated them are confirmed in the ideas which first guided them. We may give another example of this.

In 1874, in consequence of a communication addressed to the Academy of Sciences by Messrs Gosselin and A. Robin, on the subject of ammoniacal urine, we made the observation that we should endeavour to ascertain if, in all such cases, the urinary fluids were not rendered ammoniacal by the presence of the little ferment of the urea, which we have previously noticed,[27] and which has since then been discussed with remarkable intelligence by M. Van Tieghem, in the thesis which he maintained for his doctor’s degree. The suggestion and the considerations that justified it led to a discussion before the Academy of Medicine, in which contrary opinions were maintained. We lost no time in submitting these to the test of facts. We could not find a single person suffering from ammoniacal urine, in whose case the little ferment which we mentioned was not to be detected. Our predictions were thus completely justified.

As early as 1864 the _Gazette Hebdomadaire de Médecine et de Chirurgie_ published an account of urine made ammoniacal in the bladder, the author of which, Dr. Traube, makes the following observations:—“It was believed that, in consequence of the retention of the liquid, and the resulting distension of the bladder, that organ became irritated and produced a larger quantity of mucus, and that this mucus was the ferment which caused the decomposition of the urea, by virtue of a chemical action peculiar to itself. This belief can no longer be held in presence of M. Pasteur’s discoveries. This observer has demonstrated, in the most conclusive manner, that ammoniacal fermentation, like alcoholic and acetic, is produced by living beings, whose pre-existence in the fermentable liquid is a necessary condition of the process. The preceding fact offers a remarkable proof of M. Pasteur’s theory. In spite of the long duration of the retention, alkaline fermentation was not produced by an excessive secretion of the vesical mucus or of pus: it only began from the moment when the germs of vibrios passed from the outside into the bladder.”[28]

Finally, we may conclude with perfect truth that the liquids of our economy, blood and urine, for instance, may afford a harbour to different ferments, even in the inmost parts of the organs, when external causes enable such ferments to find their way into those liquids, and that diseases of greater or less gravity result from this cause. On the other hand, it must be admitted that the bodies of animals in a state of health afford no means of entrance to these external germs. At the same time, direct experiment alone can convince the mind as to the truth of this latter assertion. Let us take some of the substances that are to be found inside living animals in perfect health, and expose them, in the same condition in which life has formed them, to contact with pure air.

[Illustration: Fig. 5.]

[Illustration: Fig. 6.]

For this purpose we must provide ourselves with a glass flask, joined to a copper tap by means of an india-rubber tube, as shown in Fig. 5. The two branches of the tap should be about twelve centimetres long (about ½-in.), the one which is free tapering off like the end of a pipe. In order to destroy all germs which may exist in the flask, we must join the free end of the copper tube to a platinum tube kept at a very high temperature, after having carefully introduced into the flask a small quantity of water, and expelled all the air by converting the water into steam. Then as we allow the flask to cool, the air which re-enters it will necessarily pass through the hot tube (Fig. 6).

[Illustration: Fig. 7.]

We may cause the water in the flask to boil at a temperature of more than 100° C. (212° F.) by fitting to the free end of the platinum tube a glass tube bent at right angles, which we plunge to any depth in a deep vessel filled with mercury (Fig. 7). Whilst the water is boiling under pressure, we must separate the tube which is plunged in the mercury; the water in the flask will continue to boil at the ordinary pressure. We must then leave the flask to cool. It will gradually become filled with air that has been heated to a high temperature, more than sufficient to burn up all the organic particles of dust which that air could have contained. When the flask is cold we must close the tap and detach it, and proceed to prepare other similar flasks. It will be advisable to close the tap when the temperature of the flask is still a few degrees above that of the surrounding atmosphere: this precaution will cause the air in the cooled flask to have a lower pressure than that of the external atmosphere.

During the interval which must elapse between the preparation and the use of a flask, it is a good thing to keep the free branch of the tap inclined towards the ground, to secure the inside of its tube from the deposit of external particles of dust. Whether this precaution be adopted or not, we must take care to heat this branch in the flame of a spirit lamp just before we bring our flask into requisition.

If we have to study blood, we must take it from a living animal—a dog, for example. We must expose a vein or an artery of the animal, and make an incision into which the end of the free tap-branch, which has previously been heated and allowed to cool, must be introduced and fixed by a ligature in the vein or artery. On opening the tap, the blood will rush into the flask; it must then be closed, and the flask placed in an oven at a certain temperature. We have successfully accomplished these manipulations, thanks to the kind help of our illustrious colleague and friend, M. Claude Bernard.

The operation is nearly the same in the case of urine. The end of the free branch of the tap is introduced into the passage of the urethra; the tap is turned at the moment when the urine is emitted, which is then allowed to pass into the flask, until it is a third or half filled.

The following were the results of our experiments:—Blood underwent no putrefactive change even at the highest temperatures of the atmosphere, but retained the odour of fresh blood, or acquired the smell of lye. Contrary to what we might have expected, the direct oxidation of the constituents of blood by slow combustion was rather sluggish. After subjecting our flasks to a temperature of 25° C. or 30° C. (77° F. to 80° F.) in an oven for several weeks, we observed an absorption of not more than 2 or 3 per cent. of oxygen, which was replaced by a volume of carbonic acid gas of about an equal bulk.[29]

Nearly the same results were obtained in the case of urine; it underwent no radical change; its colour merely assumed a reddish brown tint; it formed some small deposits of crystals, but without becoming at all turbid or putrefying in any way. The direct oxidation of the urinary substances was likewise very sluggish. An analysis of the air in one of the flasks, made forty days after the commencement of the experiment, gave the following results:—

Oxygen 19·2 Carbonic acid 0·8 Nitrogen 80·0 ——- 100·0

These experiments on blood and urine which we have just mentioned date from 1863.[30] Ten years afterwards, in 1873, they were confirmed in an important and striking manner by the results of a very able series of experiments, which were carried out in our laboratory, by M. Gayon, who was formerly a pupil in the _École Normale Supérieure_. M. Gayon proved that what held good in the case of blood and urine, also held good in the case of the substances contained in eggs. He found that the whites of eggs might be exposed for any length of time to contact with air, as also might the yolks, or the white and yolks mixed, without any putrefactive change or fermentation resulting, and without the smallest microscopic germ showing itself, the sole condition being that the air must be freed from all organic particles of dust, germs of mould, _bacteria_, _vibrios_, and other organisms which it holds in suspension. This was only a part of the important facts brought to light by M. Gayon. Amongst other things, he proved that spontaneous putrefaction in eggs is invariably caused by the development of organized ferments, thereby correcting the opposite statements announced by M. Donné and M. Béchamp, who were led by their observations to believe that the change in eggs took place quite independently of the action of _vibrios_ and _mucedines_.[31]

It is almost superfluous to remark how greatly the results of these experiments on blood, urine, and the components of the egg are opposed to the doctrine of spontaneous generation, as also to most modern theories on the generation of ferments. As long as experiments relating to the question of so-called _spontaneous_ generation were made on heated substances, the advocates of _heterogenesis_ had some grounds for asserting that such materials could not satisfy the conditions of spontaneous life, and that we should obtain different results by using natural organic liquids, which, if exposed to contact of pure air would doubtless serve for the production of new beings which did not issue from parents which resembled them. This novel enunciation of the hypothesis of spontaneous generation, the only one, we think, that could be defended after the publication of our Memoir, in 1862, is condemned by the preceding facts.

The same facts completely upset the hypothesis recently maintained by Messrs. Fremy and Trécul on the subject of the causes of fermentation.

“Side by side with the immediate, definite principles which may be formed by synthesis,” says M. Fremy, “such as glucose, oxalic acid, and urea, other substances of greatly inferior stability exist, the constitution of which is considerably more complicated, containing all the elements of living organs, such as carbon, hydrogen, oxygen, nitrogen, and even phosphorus and sulphur; and often salts of lime and of the alkalies besides. These bodies are albumen, fibrin, casein, the congeners of vitellin and others. Chemical synthesis cannot reproduce them. It is impossible, in my opinion, to regard them as immediate, definite principles. I designate them by the general name of _semi-organized_ bodies, because they hold an intermediate place between the immediate principle and the organized tissue.

“These semi-organized bodies, which contain all the elements of organs, have the power, like a dry seed-grain, of existing in a state of organic immobility, and of becoming active under circumstances which favour organic development. By reason of the vital energy that they possess they undergo a succession of decompositions, giving origin to new derivatives, and to the advent of ferments, not by any process of _spontaneous generation_, but by a _vital energy_, which pre-exists in the semi-organized bodies, and is simply carried on, when this energy manifests itself, in these most varied organic changes.”

After having expressed these hypothetical and confused opinions, M. Fremy continues:—“I do not consider, then, that these semi-organized bodies serve merely as nourishment for certain animal and vegetable organisms, which may be the sole agents of fermentations, but I give them a direct _rôle_ and admit that, under the influences which I have already cited[32] they may assume a real and complete organization, and produce ferments which are not derived, as we have seen, from a germ or an ovum but from a semi-organized body, the vital energy of which has become active.[33] It will be seen that these opinions are quite different from those which M. Pasteur has maintained in his works, since they attribute the origin of alcoholic and lactic ferments to an albuminous substance. Taking the case of alcoholic fermentation alone, I assert that, in the production of wine, it is the juice of the grape itself which, in contact with air, produces grains of yeast, by the transformation of the albuminous substances. M. Pasteur, on the contrary, maintains that the grains of yeast are produced by certain germs.”[34]

We have combated these propositions, so extraordinary and unsupported by any rigorous experiments, before the Academy of Sciences, where they were first enunciated. On that occasion we related the facts in connection with blood and urine, which we have just discussed. Could there be any more forcible argument against the theory of our honourable colleague than those facts? Here we had natural albuminous substances, forming part of matter eminently liable to putrefactive change and fermentation, which produced no ferments of any sort whatsoever when brought into contact with air deprived of its organic particles of dust.

Under no known circumstances is albuminous matter transformed into grains of yeast or any other organized ferment, and, to our thinking, nothing can be more chimerical than the gratuitous hypothesis of _hemi-organism_.

We shall proceed to new proofs of this, dealing this time with a liquid formed by the life of a vegetable.

§ III.—Experiments on the Juice contained in Grapes.

In the course of the discussion which took place, at the Academy, on the subject of the generation of ferments, properly so called, much was said about the oldest known fermentation, that of wine. We at once resolved to demolish M. Fremy’s theory, by a decisive experiment on the juice of grapes.

[Illustration: Fig. 8.]

We prepared forty flasks, capable of holding from 250 c.c. to 300 c.c. (from 9 to 11 fl. oz.) and shaped as represented in Fig. 8. These we filled with filtered must, which was perfectly bright, and which, like all acid liquids, would remain sound, after having been boiled for a few seconds, although the ends of the long curved necks of the flasks containing the must might remain constantly open for months or years.

We washed, in a few cubic centimetres of water, part of a bunch of grapes, washing the grapes separately, or the grapes and the wood together, or even the wood of the bunch alone. This washing was easily accomplished by means of a perfectly clean badger’s-hair brush, the water receiving all the particles of dust adhering to the surface of the grapes and the wood of the bunch. By means of a microscope we easily proved that this water held in suspension an infinite number of organized corpuscles, some of them bearing a very close resemblance to the spores of fungoid growths, others to alcoholic ferment, others to _mycoderma vini_, and so on.[35]

[Illustration: Fig. 9.]

We next proceeded to put on one side ten of our forty flasks, to serve for subsequent corroboration; in ten others, by means of the tube which is represented on the right hand side of the flask (Fig. 8), we put a few drops of the water in which the bunch of grapes had been washed; in a third series of ten flasks we put a few drops of the same liquid, after having previously boiled it. Lastly, we introduced into the ten remaining flasks a drop of grape-juice, taken from the inside of an uninjured grape. To do this we had to bend the right-hand tube of each of our last ten flasks, drawing it out to a fine point and closing it in the flame, as represented in Fig. 9 A. This fine closed point was filed round near its extremity and then thrust, as represented in Fig. 9 B, into a grape placed on a hard substance; when the point _b_ was felt to touch the substance supporting the grape it was broken off by a slight pressure sideways at the point _a_, where the file marks had been made. We had taken care to secure a slight vacuum in the flask beforehand; this now caused a drop of the juice to be drawn into the flask. We then drew out the fine point, and closed it immediately in the flame of a spirit lamp. The vacuum was produced by heating the flasks in our hands, or over the flame of a lamp, thus causing a little air to be forced out through the end of the bent tube, which we then closed up with the lamp. When the flask was cool, the slight difference of pressure sufficed to force into it some of the juice contained in the grape, as we have just described. The drop of juice that is sucked into the flask generally remains in the curved part of the fine tube; to mix it with the must we must incline the flask so as to bring the must in contact with the drop; after that we may replace the flask in its natural position.

The following are the results presented by our four series of comparative experiments in the different cases. The first ten flasks—our standard flasks, containing must boiled in contact with pure air—showed no signs of organized products; the must might have remained in them for any number of years without change. Our second series of flasks, which contained the water in which the grapes, separately and in bunch, had been washed, had undergone alcoholic fermentation in every instance; this had manifested itself in all the flasks in the course of about forty-eight hours, the temperature being at about summer heat. At the same time that the yeast made its appearance in the form of little white lines, which gradually joining together formed a deposit on the sides of the flask, we perceived minute flakes of _mycelium_ forming; sometimes as a single fungoid growth, sometimes combined with another, or with many together—these growths being quite independent otherwise of the yeast or alcoholic ferment. In several cases, too, _mycoderma vini_ showed itself on the surface of the liquid in the course of a few days. _Vibrios_ and lactic ferments, properly so called, could not make their appearance, on account of the nature of the liquid.

The flasks of our third series, containing the water in which the bunch of grapes had been washed, and which we boiled before our experiment, remained as free from change as the flasks of our first series had done.

Lastly, our fourth series of flasks, containing the drops of juice taken from inside the grapes, remained equally free from change, although we could not be certain of having removed, in every case, without exception, all causes of error which must inevitably occur sometimes in so delicate an experiment.

These experiments cannot leave the least doubt on our minds:

That must, if boiled, will never ferment when in contact with air that has been freed from the germs which exist in it in a state of suspension.

That must may be fermented, after boiling, by introducing into it a very small quantity of water, in which a bunch of grapes has been washed.

That must will not ferment if we introduce into it some of this same water which has been boiled and afterwards cooled.

That must will not ferment if we introduce into it a small quantity of the juice contained in a grape.[36]

It follows, then, that the ferment which causes grapes to ferment in the vintage tub must come from the exterior, and not the interior of the grapes. Thus, the hypothesis of MM. Trécul and Fremy, according to which albuminous substances transform themselves into grains of yeast by the

## action of a peculiar vital force, is annihilated; _à fortiori_, there

can no longer be a question concerning Liebig’s theory, on the transformation of albuminous substances into ferments, by a process of oxidation.

Our readers may be curious to know what M. Fremy has been able to oppose to such crucial experiments; they could scarcely have imagined the following:—

“In my experiments, which I have varied in every possible manner,” says that gentleman, “I have found that it is almost impossible to discover alcoholic fermentation, appreciable by its results, in a single drop of grape juice, and I may add that this fermentation must be still more difficult to discover when this drop has been drowned in a large quantity of juice that has been previously boiled.”[37]

It will be admitted that we were justified in saying, at the commencement of this paragraph, that we should demolish the theory which was opposed to ours, and which its advocates have been constrained to defend by hypotheses manifestly false.

At the meeting following the one in which M. Fremy declared _that minute quantities do not ferment_, we had the malicious satisfaction of showing a great many very small closed flasks, into each of which we had caused a single drop of the must of crushed grapes to be introduced by suction. We broke the thin points of many of them, in the presence of the Academy, and every one of them showed by a sharp hissing, which was audible at a distance, that fermentation was proceeding in the drop of liquid they contained. M. Fremy was there, but he made no remark.

We may cite some very curious facts on the subject of the period at which the germs that develop yeast are in a condition to be able to cause fermentation.

On July 25th, 1875, in the neighbourhood of Arbois (Jura), the grapes were still green and of the size of peas. We went to a vine that was far from paths and roads, and there, with a pair of small scissors, cut some grapes from off a bunch and let them fall with their short stalks into tubes half filled with gooseberry must, previously rendered unalterable by boiling. These tubes we closed again with all possible precautions, using corks which had been passed through the flame of a spirit-lamp and carried them to our laboratory, where we left them to themselves. Some days afterwards we saw diverse fungoid growths appear in most of the tubes, but not one of them then, or subsequently, presented the least appearance of fermentation. The germs of yeast at that period of the year did not exist either upon the woody part of the bunch, or upon the grapes. In