Memoire sur les corpuscules organisés qui existent dans l'atmosphère. Examen de la doctrine des générations spontanées.
(Memoir on the organized bodies which exists in the atmosphere. Examination of the doctrine of spontaneous generation.)
by Louis Pasteur, published 1862, here Google-translated to English. The original text is available at https://archive.org/details/s696id13664800/page/5/mode/1up.
(Not all of the original footnotes are included in this translation.)
Contents:
Chapter 1. Historical background.
Chapter 2: Microscopic examination of disseminated solid particles in atmospheric air.
Chapter 3: Experiments with heated air.
Chapter 4: Sowing of dust that exists in suspension in the air, in liquors which permit the development of lower organisms.
Chapter 5: Extension of the previous results to new, highly deteriorable liquids. –Urine. –Milk. –Sugar albuminous water mixed with calcium carbonate.
Chapter 6: Another simple method to demonstrate that all organized productions of infusions (previously heated) originate from the particles that exist in suspension in atmospheric air.
Chapter 7: It is not true that the smallest quantity of ordinary air is sufficient to give rise, in an infusion, to the organized productions [microorganisms] specific to that infusion. –Experiments on air from various locations. –Drawbacks of using a mercury bath in experiments related to so-called spontaneous generation.
Chapter 8: Comparative action of temperature on the fertility of spores of Mucedinea and germs that exist in suspension in the atmosphere.
Chapter 9: On the mode of nutrition of the ferments properly so-called, of the Mucedins and Vibrios.
CHAPTER 1. Historical background.
In antiquity and until the end of the Middle Ages, everyone believed in the existence of spontaneous generation. Aristotle said that any dry body that becomes wet and any wet body that dries out will give rise to animals. Van Helmonl described how to breed mice. Many authors still indicated in the 17th century how to breed frogs from marsh silt, or eels from the water of our rivers. Such errors could not long withstand the spirit of inquiry that gripped Europe in the 16th and 17th centuries. Redi, a famous member of the Accademia del Cimento, demonstrated that the worms in rotting flesh were fly larvae. His proofs were as simple as they were decisive, for he showed that simply wrapping rotting flesh in fine gauze was enough to absolutely prevent the birth of these larvae. Redi was also the first to recognize males, females, and eggs in the animals that live in other animals. These flies that lay their eggs in fruit were caught in the act, Réaumur later said, and it was understood, when a worm was seen in an apple, that it was not the rot that had engendered it, but rather that the worm was the cause of the fruit's decay.
But soon, in the second half of the 17th century and the first half of the 18th, microscopic observations proliferated. The doctrine of spontaneous generation then reappeared. Unable to explain the origin of these diverse organisms revealed by the microscope in infusions of plant or animal matter, and seeing nothing resembling sexual generation in them, some were led to believe that matter which had once lived retained its own vitality after death, under whose influence its disjointed parts reunited, under certain favorable conditions, with variations in structure and organization determined by those very conditions. Others, on the contrary, adding to the marvelous results revealed by the microscope through their imagination, believed they saw mating in these infusoria—males, females, eggs—and positioned themselves as declared opponents of spontaneous generation. It must be admitted that the evidence supporting either of these opinions hardly stood up to scrutiny.
The question stood at this point when, in 1745, a work by Needham appeared in London. Needham was a skilled observer and a devout Catholic priest, a circumstance which, in such a subject, seemed to guarantee the sincerity of his convictions. In this work, the doctrine of spontaneous generation was based on facts of an entirely new kind: experiments on hermetically sealed vessels, previously exposed to the effects of temperature. It was Needham, in fact, who first conceived of such experiments. No sooner had Needham's research been published than the Royal Society of London admitted him as a member. Later, he became one of the eight associates of the Academy of Sciences. But it was above all through the support he received from Buffon's system of generation that Needham's work had such a significant impact.
The first three volumes of Buffon's quarto edition, published during his lifetime, appeared in 1749. It was in the second volume of this edition, four years after Needham's book, that Buffon presented his system of organic molecules and defended the hypothesis of spontaneous generation. It is likely that Needham's findings had a significant influence on Buffon's views, for it was at the very time when the illustrious naturalist was writing the first volumes of his work that Needham traveled to Paris, during which he was Buffon's companion and, in a sense, his collaborator.
Needham and Buffon's ideas had their supporters and detractors. They were in opposition to another famous system, that of Bonnet, concerning the pre-existence of germs. The debate was all the more intense because it might have seemed more legitimate to both sides. We know today that the truth lay neither on one side nor the other. And besides, it was still a time when people readily debated endlessly on systems and speculative views.
There were, in a way, two men of opposing minds in Buffon: one who today would readily admit that he was seeking a hypothesis to construct a system, and who, the next day, would write the beautiful preface to his translation of Hales's Chemical Statics of Plants, where the necessity of experimentation is given due weight. These two facets of Buffon's genius can be found, to varying degrees, in all the scientists of his time. But Needham's conclusions were soon subjected to experimental verification. At that time in Italy, there was one of the most skilled physiologists science could boast, the most ingenious, the most difficult to satisfy: Abbé Spallanzani.
Needham, as I mentioned earlier, had based the doctrine of spontaneous generation on very well-conceived direct experiments. Experience alone could either condemn or absolve his opinions. This is what Spallanzani understood very well. “In several Italian cities,” he said, “parties have been formed against Mr. de Needham’s opinion, but I do not believe that anyone has ever thought to examine it experimentally.”
In 1765, Spallanzani published a dissertation in Modena in which he refuted the systems of Needham and Buffon. This work was translated into French, probably at Needham’s request, because the edition published in 1769 includes notes written by Needham, in which he responds to all of Spallanzani’s objections. The latter, undoubtedly struck by the accuracy of Needham's criticisms, returned to the work and soon published this fine collection of studies, the details of which he transmitted to us in his *Opuscules physiques* (1).
It would be pointless to present a complete history of the quarrel between the two naturalists. But it is important to specify the experimental difficulty to which they particularly applied their efforts, and to investigate whether this long debate had dispelled all doubts. This is what is generally believed. Spallanzani is readily regarded as Needham's victorious adversary. If this judgment were well-founded, should we not be surprised that there are still so many proponents of the doctrine of spontaneous generation today? In the sciences, is not error more readily dispelled, even in questions of this kind, when it has been truly exposed by experiment? Is it not to be feared, if we see it revived in good faith, that its defeat was only apparent?
An impartial examination of the contradictory observations of Spallanzani and Needham on the most delicate point of the subject will show us, in fact, contrary to the generally accepted opinion, that Needham could not in all fairness abandon his doctrine in the face of Spallanzani's work.
I said that Needham was the author of the experiments relating to what is observed in sealed vessels, previously exposed to the action of fire. “Mr. de Needham,” says Spallanzani, “assures us that the experiments thus arranged have always been very successful in his hands; that is to say, the infusions have shown the presence of infusoria, and that this is what sealed his system.” “If, after purging,” adds Spallanzani, “by means of fire, both the substances placed in the vessels and the air contained within them, one takes the further precaution of removing all communication with the surrounding air, and if, despite this, upon opening the vials, one still finds living animals, this will become strong proof against the ovarian system. I don't even know what his supporters will be able to say in response.”
I emphasize these last words to show that Spallanzani placed the criterion of truth or error in the results of the experiments thus conducted. Now, we will see from the following quotation, taken from Needham's notes, that this was also his opinion. Here, in fact, is a passage from Needham's remarks on Chapter X of Spallanzani's first dissertation: "It only remains for me," says Needham, "to speak of Spallanzani's last experiment, which he himself considers the only one in his entire dissertation that seems to have any force against my principles.
He hermetically sealed nineteen vessels filled with different plant substances, and boiled them, thus sealed, for the space of an hour. But from the way he treated and subjected his nineteen herbal infusions, it is clear that he not only greatly weakened, or perhaps completely destroyed, the vegetative force of the infused substances, but also that he entirely corrupted, through exhalations and the heat of the fire, the small portion of air that remained in the empty part of his flasks. It is therefore not surprising that his infusions, thus treated, showed no sign of life. It was bound to be so.
Here, then, is my last proposal and the result of all my work in a few words: Let him, by renewing his experiments, use substances sufficiently cooked to destroy all the so-called germs believed to be attached either to the substances themselves or to the inner walls, or floating in the air of the vessel; let him seal his vessels hermetically, leaving a certain portion of air inside without disturbing it; let him then plunge them into boiling water for a few minutes, only the time it takes to harden a hen's egg and to kill the germs; in short, let him take all the precautions he wants, provided that he seeks only to destroy the so-called foreign germs that come from outside, and I answer that he will always find these microscopic vital beings in sufficient number to prove my principles.
If, upon opening his vessels, after allowing them to rest for the time necessary for the formation of these bodies, he finds nothing vital nor any sign of life, then, conforming to these conditions, I will abandon my system and renounce my ideas. This, I believe, is all a judicious opponent can demand of me.
This, admittedly, is the clearly limited discussion between Needham and Spallanzani. It is in Chapter III of Volume I of his Opuscules that Spallanzani addresses the decisive difficulty. And what is his conclusion? To eliminate all production of infusoria, it is necessary to maintain the infusions at a near-boiling temperature for three-quarters of an hour (1).
Footnote: (1) “I succeeded,” said Spallanzani, “in obtaining vessels that withstood the action of fire better, and I managed to subject them to a longer boiling, by putting in only a small dose of the infusions I had mentioned. Without this precaution, I was still certain to see all my vessels explode. But, so as not to waste precious time on overly small details, I will only report the result of my observations. Boiling for half an hour was not an obstacle to the birth of the lowest-order animalcules, which always populated more or less all the vessels exposed to its action for that entire time; but boiling for three-quarters of an hour, or even for a slightly shorter time, had the power to completely deprive the six infusions of animalcules” (Spallanzani, Opuscules, vol. I, p. 39).
Now, did this required duration of a temperature of 100°C for three-quarters of an hour not justify Needham's fears about a possible alteration of the air in the vessels? At the very least, Spallanzani should have included an analysis of this air in his experiments. But science was not yet sufficiently advanced; eudiometry had not yet been developed. The composition of atmospheric air was barely known (2).
Footnote: (2) Spallanzani’s first dissertation dates from 1763. His Opuscules were first published in 1776. Lavoisier’s discovery of the composition of air dates from 1774.
The results of Spallanzani's experiments on the most delicate point of the question thus preserved the full validity of Needham's objections. Moreover, these objections were legitimized, at least superficially, by subsequent scientific progress.
Appert applied the results of Spallanzani's experiments, conducted according to Needham's method, to domestic economy. For example, one of the Italian scientist's experiments consisted of placing peas and water in a glass vessel, which was then hermetically sealed, and subsequently kept in boiling water for three-quarters of an hour. This was indeed Appert's method. Gay-Lussac, wishing to ascertain the method, subjected it to various tests, the results of which he recorded in one of his most frequently cited memoirs.
The following extracts from Gay-Lussac's work leave no doubt as to one of the illustrious physicist's opinions, an opinion that has become widely accepted and unchallenged throughout the scientific community. "One can be convinced," says Gay-Lussac, "by analyzing the air in the bottles in which the substances (beef, mutton, fish, mushrooms, grape must) have been well preserved, that it no longer contains oxygen, and that the absence of this gas is consequently a necessary condition for the preservation of animal and vegetable substances.”
Let us consider only the first part of Gay-Lussac’s assertion, namely, that there is no longer any oxygen in Appert’s preserves. Do you not see that this justifies Needham’s fears about an alteration of the air in the vessels in Spallanzani’s experiments? As I said earlier, consequently, Spallanzani had not overcome Needham’s objections.”
But an experiment by Schwann brought about a very significant advance in the matter. In February 1837, Mr. Schwann published the following facts: An infusion of muscle tissue is placed in a glass flask, the flask is then sealed with a lamp, and then exposed entirely to boiling water. After cooling, it is left to its own devices. The liquid does not putrefy. Up to this point, nothing particularly new. It is one of Spallanzani's experiments, or rather a preservation of Appert's.
But it was desirable, adds Mr. Schwann, to modify the experiment in such a way that a renewal of the air became possible, with the condition, however, that the new air be preheated as the air in the flask was originally.
Then Mr. Schwann repeated the previous experiment, fitting a stopper with two holes in the neck of the flask. These holes were pierced by bent and curved glass tubes, so that their curves were immersed in baths of fusible alloy maintained at a temperature close to that of mercury boiling. Using [an aspirator], the air was renewed; it arrived cold in the flask, but had been heated by passing through the portion of the tubes surrounded by the fusible alloy. He began the experiment by boiling the liquid. The result was the same as in the experiments of Spallanzani and Appert. There was no alteration of the organic liquid. The air, heated and then cooled, thus left meat juice that had been brought to a boil intact.
This was a great advance, because it vindicated Spallanzani's argument against Needham. This addressed all of the latter's concerns about the possible alteration of the air in Spallanzani's experiments; it finally refuted Gay-Lussac's assertion regarding the role of oxygen in Appert's preserving processes and in alcoholic fermentation. However, on this last point, some doubts remained—in fact, in this same work by Sehwann, besides the experiment on meat broth, which touched upon the cause of putrefaction, there is another related to alcoholic fermentation, which should be mentioned.
The author filled four flasks with a solution of cane sugar mixed with brewer's yeast; then, after tightly sealing them, he placed them in boiling water and then placed them over the mercury bath. After they had cooled, he introduced air into them: ordinary air into two of them, and [heated] air into the other two. After a month, fermentation had occurred in the flasks that had received ordinary air; it had not yet appeared in the other two after two months of waiting. “But in repeating these experiments”, he said, “I found that they are not always so successful, and that sometimes fermentation does not occur in any of the flasks, for example, when they have been kept too long in boiling water, and sometimes, on the other hand, the liquid ferments in the flasks that have received heated air.”
In summary, Dr. Schwann's experiment concerning the putrefaction of broth is very clear. However, regarding alcoholic fermentation, the only fermentation that was reasonably well understood in 1837, at the time of Mr. Schwann's work, the experiments of the learned physiologist were contradictory, and yet it had just been learned, through the observations of Mr. Cagniard de Latour and those of Mr. Schwann himself, that wine fermentation was determined by an organized ferment.
How much more were these obscurities of the question, with regard to alcoholic fermentation, increased when, subsequently, chemists studied a large number of fermentations where no organized ferment could be discovered, and whose cause was universally attributed to contact actions, phenomena of entrainment or transmitted movement produced by dead nitrogenous matter in the process of alteration.
In any case, here is the conclusion that Dr. Schwann deduced from the experiments I have just reported: “For alcoholic fermentation,” he said, “as for putrefaction, it is not oxygen, at least not atmospheric oxygen alone, that causes them, but a principle contained in ordinary air, which heat can destroy.” The reservation in this conclusion deserves to be noted. It is clear from certain passages in his work that Dr. Schwann was inclined to believe that, through heat, he destroyed germs; but his final conclusion could not and does not go that far. Often, in reporting their experiments, opponents of the doctrine of spontaneous generation have asserted that the use of heat had no other purpose than to kill germs; but this was only a hypothesis. As Dr. Schwann so aptly put it, these experiments only prove that it is not oxygen, or at least not oxygen alone, that is the cause of putrefaction and wine fermentation, but something unknown that heat destroys. And even then, for wine fermentation, it was not well established that it was necessary to resort to a cause other than that indicated by Gay-Lussac, namely, oxygen alone in the air (1).
Dr. Schwann's experiments were repeated and modified by several observers. Messrs. Ure and Helmholtz (2) confirmed his results with experiments similar to his own. Mr. Schultze, instead of calcining the air before placing it in contact with Appert's preserves, passed it through chemical reagents: concentrated potash and sulfuric acid. Schröder and Dusch imagined filtering the air through cotton, instead of modifying it by a high temperature in the manner of Doctor Schwann, or by energetic chemical reagents, according to the process of Mr. Schultze (1).
The first Memoir by Messrs. Schröder and Dusch appeared in 1854, the second in 1839. These are excellent works, which also have the historical merit of showing the state of the question at hand in 1859. It had long been known, from the very first discussions on spontaneous generation, that a fine gauze, already used with such success by Redi in his research on the origin of larvae in rotting meat, was sufficient to prevent, or at least to significantly modify, the spoilage of infusions. This very fact was among those most frequently invoked at the time by the opponents of the doctrine of spontaneous generation (1).
Footnote: (1) Extract from a passage in the work of Baker, member of the Poetic Society of London, entitled: The Microscope Within Everyone's Reach, translated from the English edition of 1743. Paris, 1754. “I have consistently found that if a pile (of pepper, of hay) is covered with muslin or another fine cloth, very few animals appear on it, but that if this covering is removed, it is full of life within a few days… As the eggs of these little creatures are less heavy than… it can happen that millions of them are continually released into the air, and that, being carried indiscriminately from all sides, a great number perish in places unsuitable to their nature… There are people who imagine that the eggs of these little animals are lodged in pepper, in hay, or in all the other materials that are put in water; but if that were the case, I could not understand how such a small covering of fine cloth, which does not prevent pepper from penetrating, could prevent these eggs from hatching: one must conclude that this is an illusion.”
Guided no doubt by these facts, and especially, as they expressly state, by the ingenious experiments of Mr. Loevel, who recognized that ordinary air was unsuitable for causing the crystallization of sodium sulfate when filtered through cotton, Messrs. Schröder and Dusch proceeded as follows:
A glass flask receives the organic matter. The flask's stopper is pierced by two tubes bent at right angles: one of these tubes connects to a water aspirator, the other to a large tube 1 inch in diameter and 20 inches long filled with cotton. Once the connections were well established, the aspirator's valve closed, and the organic matter placed in the flask, the latter was heated until boiling, maintaining the boiling point for a sufficient time so that all the connecting tubes were thoroughly heated by the steam; then we would open the tap of the [aspirator] which we maintained day and night.
Here are the results of the first tests conducted in this manner:
Messrs. Schröder and Dusch performed the following experiments:
1. On meat with added water,
2. On beer wort,
3. On milk,
4. On meat without added water.
In the first two cases, the air filtered through cotton left the liquids intact, even after several weeks. But the milk curdled and rotted as quickly as in ordinary air, and the meat without water quickly began to putrefy.
"It therefore seems to follow from these experiments," say Messrs. Schröder and Dusch, "that there are spontaneous decompositions of organic substances that require only the presence of oxygen gas to begin; for example, the putrefaction of meat without water, the putrefaction of casein in milk, and the transformation of milk sugar into lactic acid (lactic fermentation)." But alongside these, there would be other phenomena of putrefaction and fermentation wrongly placed in the same category as the former, such as the putrefaction of meat juice and alcoholic fermentation, which would require, in addition to oxygen, those unknown substances mixed with atmospheric air, which are destroyed by heat according to Schwann's experiments, and according to ours, by filtering this air through cotton. As so many questions remain to be resolved experimentally, we will refrain from drawing any theoretical conclusions from our experiments.
Mr. Schröder returned to this subject alone in 1859, in a Memoir which also deals with the cause of crystallization. This new work did not lead its author to conclusions free from all uncertainty; He describes new organic liquids that do not putrefy when placed in contact with filtered air, such as urine, starch glue, and various materials of milk taken in isolation; but he adds egg yolk to the list of substances that, like milk and meat without water, putrefy in air filtered through cotton.
“I will not venture,” said Mr. Schröder, “to attempt a theoretical explanation of these facts. One could admit that fresh air contains an active substance that causes the phenomena of alcoholic fermentation and putrefaction, a substance that heat would destroy, or that cotton would stop.” Then he added: “Should we consider this active substance as formed from microscopic organized germs disseminated in the air? Or is it a chemical substance as yet unknown? I don’t know.”
Then he came to the phenomena of crystallization by open air, by hot air, or by air filtered through cotton, which, according to him, present such analogies with the phenomena of putrefaction that he cannot help but attribute them to a common cause hitherto entirely unknown.
“As for crystallization,” he continued, “the inductive action of air does not appear to be completely stopped by cotton, but only weakened. It can then only prevent the crystallization of certain supersaturated solutions; but there are others that cannot resist it.” He then noted that the results he obtained on putrefaction and fermentation paralleled those of crystallization, since some substances resist filtered air, while others, such as milk, decompose. Air filtered through cotton, therefore, only partially loses its inductive force for putrefaction or fermentation.
I have deliberately summarized these very judicious works in detail, because they accurately express the difficulties which, in 1859, must have beset any impartial mind, free from preconceived ideas, and eager to form a duly reasoned opinion on this serious question of spontaneous generation.
It can be stated that at that time all those who believed it resolved were poorly informed about its history. Spallanzani had not overcome Needham's objections, and Messrs. Schwann, Schultze, and Schröder had only demonstrated the existence in atmospheric air of an unknown principle that was the condition for life in infusions. Those who asserted that this principle was nothing more than germs had no more proof to support their opinion than those who thought it could be a gas, a fluid, miasmas, etc., and who, consequently, were inclined to believe in spontaneous generation. The conclusions of Messrs. Schwann and Schröder cannot, in this respect, leave the slightest doubt in the reader's mind. The very wording of these conclusions provoked doubt and served the doctrine of spontaneous generation.
Furthermore, the experiments of Messrs. Schwann, Schultze, and Schröder were successful only with certain liquids. Moreover, they failed almost constantly and with all liquids, as I will soon explain, when they were performed on the mercury bath, without anyone knowing the reason for this failure or being able to identify any cause of error.
Thus, when (1), after the work I have just mentioned, a skilled naturalist from Rouen, Mr. Pouchet, a corresponding member of the Academy of Sciences, came to announce to the Academy results on which he believed he could definitively establish the principles of [spontaneous generation], no one could point to the true source of error in his experiments, and soon the Academy, understanding all that still remained to be done, proposed the following question as a prize topic: To attempt, through well-conducted experiments, to shed new light on the question of spontaneous generation (1).
Footnote: (1) The Commission was composed of Messrs. Geoffroy-Saint-Hilaire, Brongniart, Milne Edwards, Serres, and Flourens (rapporteur). “The Commission requests precise, rigorous experiments, equally studied in all their circumstances, and such, in short, that a result can be deduced free from any confusion arising from the experiments themselves.” (January 1860.) Such was the Commission’s program. The difficulties of the subject could not have been better indicated.
The question then seemed so obscure that Mr. Biot, whose kindness had never faltered in my studies, watched with regret as I embarked on this research and, out of deference to his advice, demanded that I accept a time limit, beyond which I would abandon the subject if I could not overcome the difficulties that hindered me. Mr. Dumas, whose kindness had often conspired with Mr. Biot's in matters concerning me, told me at the same time: "I would advise no one to remain too long on this subject."
What need did I have to pursue it? For the past twenty years, chemists have discovered a set of truly extraordinary phenomena, designated by the generic name of fermentations. All require the participation of two substances: one fermentable, such as sugar, and the other nitrogenous, which is always an albuminoid substance [albuminoid = albumin-like, or egg white-like, i.e. a substance rich in protein].
Now here is the theory which was universally accepted: albuminoid substances, when exposed to contact with air, undergo an alteration, a particular oxidation, of unknown nature, which gives them the fermenting character, that is to say the property of then acting, by their contact, on fermentable substances.
There was indeed one ferment, the oldest and most remarkable of all, known to be organized: brewer's yeast. But as in all fermentations discovered more recently than the knowledge of the fact of the organization of brewer's yeast (1836), the existence of organized beings had not been detected, even when carefully searching for them, physiologists had gradually abandoned, many with great regret, the hypothesis of M. Cagniard de Latour, of a probable relationship between the organization of this ferment and its property of being a ferment, and the general theory was applied to brewer's yeast, saying: “It is not because it is organized that brewer's yeast is active, it is because it has been in contact with air. It is the dead portion of the yeast; that which has lived and is in the process of alteration that acts on the sugar.”
My studies led me to entirely different conclusions. I found that all true fermentations—viscous, lactic, butyric, the fermentation of tartaric acid, malic acid, and urea—were always correlated with the presence and multiplication of organized organisms. And, far from the organization of brewer’s yeast being a hindrance to the theory of fermentation, it was precisely through this organization that it fell within the common law and became the type of all true ferments. In my view, albuminoid substances were never ferments, but rather the food of ferments. True ferments were organized organisms.
That being said, ferments originate, as we know, through the contact of albuminoid substances and oxygen gas. Therefore, I reasoned, one of two things must be true: since the ferments of fermentation proper are organized, if oxygen alone, as oxygen, gives rise to them through its contact with nitrogenous substances, these ferments are spontaneously generated; if these ferments are not spontaneous beings, it is not as oxygen alone that this gas intervenes in their formation, but as an activator of a germ introduced at the same time, or existing within the nitrogenous or fermentable substances.
At this point in my studies of fermentation, I therefore had to form an opinion on the question of spontaneous generation. Perhaps I would find there a powerful argument in favor of my ideas on fermentation proper. The research I am now about to report was therefore merely a necessary digression from my studies on fermentation. This is how I came to concern myself with a subject that, until then, had only engaged the sagacity of naturalists.
CHAPTER 2: Microscopic examination of disseminated solid particles in atmospheric air.
My first concern was to find a method which would allow the collection, in all seasons, of the solid particles which float in the air and to study them under the microscope. It was necessary first to address, if possible, the objections which the proponents of spontaneous generation raise against the old hypothesis of the airborne dissemination of germs.
When the organic matter in infusions has been heated, it becomes populated with infusoria or molds. These organized growths [microorganisms] are generally neither as numerous nor as varied as if the liquids had not been previously boiled, but they always form. Now, their germs, under these conditions, can only come from the air, because boiling destroys those that the vessels or the materials of the infusion have introduced into the liquid.
The first experimental questions to be resolved are therefore these: Are there germs in the air? Are there enough of them to explain the appearance of organized growths in infusions that have been previously heated? Can we get an approximate idea of the relationship between a given volume of ordinary air and the number of germs that this volume of air can contain?
First, do germs exist in the air? No one denies it, because it is understood that it cannot be otherwise. One of the most outspoken proponents of the doctrine of spontaneous generation, Mr. Pouchet, expresses himself in the following way:
“One sometimes finds in dust a few eggs of Microzoa [“microscopic animals”, here used (I believe) to refer to motile microorganisms, not necessarily classified as animals in modern biology], just as one finds a multitude of light corpuscles, but this is a true exception.”
Further on, Mr. Pouchet expresses himself thus: “Among the dust corpuscles that belong to the plant kingdom, there are spores of Cryptogams, but in very small numbers. Finally, I have constantly encountered a certain quantity of wheat starch mixed with dust, whether recent or old... It is evident that [it is] this starch, perfectly characterized physically and chemically, or that [it is] grains of silica that have been mistaken for Microzoan eggs.”
Therefore, in the dust of the air there are eggs of fungi and spores of molds; the proponents of the doctrine of heterogenesis [spontaneous generation] affirm this; but they add that they are only found exceptionally, in extremely small numbers, and those who, they say, believed they saw more were mistaken. They were unaware of a recent fact, namely that there are grains of starch of various sizes in the dust. These observers mistook these grains of starch, which often so closely resemble them, for eggs or spores.
Such is Mr. Pouchet's opinion. I have not made enough observations on ordinary dust deposited on the surface of objects to be able to refute this assertion concerning dust at rest. I can even add that at the time I conducted my first experiments, several highly authoritative individuals were eager to verify the accuracy of my results for themselves, because, they told me, having had frequent opportunities to study dust, they had not observed any spores in it.
But here a point needs to be made: the dust found on the surface of all bodies is constantly subjected to air currents that must lift its lightest particles, among which are undoubtedly, and perhaps primarily, the organized corpuscles, eggs or spores, generally lighter than mineral particles. Furthermore, with regard to ordinary dust at rest, it is impossible to determine the approximate ratio that may exist between a given volume of this dust and the volume of air that produced it. Therefore, it is not the dust at rest that should be observed, but rather that which is suspended in the air.
Let us see if this is feasible, and if it is true that this floating dust only exceptionally contains germs of lower organisms, as is the case, according to Mr. Pouchet, with dust at rest. The method I followed for collecting dust suspended in the air and examining it under a microscope is very simple; it consists of filtering a determined volume of air through nitrocellulose, soluble in a mixture of alcohol and ether. The nitrocellulose fibers trap the solid particles. The nitrocellulose is then [dissolved in solvent]. After a sufficiently long resting period, all the solid particles settle to the bottom of the solution; they are subjected to a few washes, then placed on the microscope slide, where their study becomes easy.
[The word Pasteur uses for his dust-filter is “coton-poudre”, which Google translates to “powdered cotton”. Thomas Brock, in his book “Milestones in Microbiology”, translates “coton-poudre” to guncotton. This translation is correct, according to https://www.cnrtl.fr/definition/coton-poudre. Guncotton is a synonym of nitrocellulose, and I will be translating “coton-poudre” to nitrocellulose.]
I will now go into the details of the experiment: “FF”, Fig. 1, Plate I, is a window frame in which I had made an opening, several meters above the ground, allowing passage of the glass tube "T". In my experiments, this tube was only half a centimeter in diameter. At "a" is a wad of nitrocellulose, about one centimeter long, held in place by a small platinum wire spiral. The air, which was ordinarily drawn in from the direction of the Rue d'Ulm or the garden of the École Normale, was drawn in by the aspirator "R". This is a T-shaped brass tube into which water constantly flows, and which, by suction, draws the air from the tube "mn", slightly curved at its end "n", as shown in the figure. Tube "mn" is connected via a rubber tube to tube "T" containing the soluble cotton wadding.
To determine the volume of air carried along by the flow of water, simply place the end "l" of tube "kl" under a large inverted flask filled with water, pre-filled, and measure the time it takes for this flask, with a volume of 10 liters for example, to fill. [I assume he means that this large flask is to be inverted under a pool of water, and the tube “kl” is to enter the pool, with the end “l” just inside the opening of the flask.]
This method of continuous suction is very convenient and has been of great service to me. After the air has passed through for a sufficient time, the cotton wadding, more or less soiled by the dust it has trapped, is placed in a small tube with the alcoholic ether mixture that dissolves the cotton. It is left to stand for a day. All the dust collects at the bottom of the tube, where it is easy to wash it by decantation, without any loss, provided that care is taken to separate each washing with a resting period of twelve to twenty hours. To decant the liquid, it is advisable to use a siphon formed by a tube of very small diameter, which can be primed by suction.
[By “washing” the dust, I think Pasteur means the removal of the previous ether-alcohol-mixture and addition of new ether-alcohol-mixture. My best guess is that this wash-process is necessary to get rid of all the nitrocellulose.]
When the dust has been sufficiently washed, it is collected in a watch glass [a circular concave glass] where the remaining liquid surrounding it evaporates quickly (1); then it is rinsed in a little water and examined under a microscope.
Footnote: (1) Washing is sufficient after five or six decantations. One must use cotton with the highest possible solubility.
Various reagents can be applied to [the dust particles] using ordinary methods: iodine solution, potassium solution, sulfuric acid, and coloring agents. These very simple manipulations allow us to recognize that there is constantly a variable number of particles in the common air, whose shape and structure indicate that they are organized. Their dimensions range from the smallest diameters up to 1/100 to 1.5/100 and more millimeters. Some are perfectly spherical, others ovoid. Their outlines are more or less clearly defined. Many are completely translucent, but there are also opaque ones with internal granulations. Those that are translucent, with sharp outlines, so closely resemble the spores of the most common molds that the most skilled micrographer could not distinguish them.
That is all that can be said about them, just as one can only affirm that, among the others, some resemble encysted, ball-shaped Infusoria, and generally the globules that are considered to be the eggs of these small organisms. But as for asserting that this is a spore, moreover the spore of a specific species, and that this is an egg, and the egg of a specific Microzoan, I believe that this is not possible. I confine myself, as far as I am concerned, to declaring that these corpuscles are evidently organized, resembling in every respect the germs of the lowest organisms, and so diverse in size and structured that they undoubtedly belong to a great many species.
The use of iodine water shows in the least ambiguous way that, among these corpuscles, there are always granules of starch. But it is quite easy to eliminate all globules of this kind by diluting the dust in ordinary sulfuric acid, which dissolves all starch in a few moments. Undoubtedly, sulfuric acid alters, and perhaps dissolves, other globules; but a large number still remain, and sometimes even more are distinguishable after the action of sulfuric acid, because this acid dissolves calcium carbonate and dilutes the other dust particles, so that many organized corpuscles are freed from the amorphous debris that often prevents them from being seen clearly. It is advisable to observe immediately after the small bubbles of carbonic acid have dissipated, and before the needles of calcium sulfate have settled (1).
Footnote: (1) I have determined, through direct tests, that ordinary sulfuric acid does not dissolve the spores of common molds, even with prolonged contact.
By operating on the dust of a wad 1 centimeter long by 1/2 centimeter in diameter, exposed to an air current for twenty-four hours, with a flow of one liter per minute, one can easily discover and draw twenty to thirty organized corpuscles in a quarter of an hour. There are usually several in the field of view [of the microscope]. Note that the drop of acid mixed with dust, which is placed on the microscope slide, represents only a fraction of the drop in the watch glass.
On the other hand, it would obviously take several hours to search for and draw, step by step, all the organized corpuscles in this drop. We can see, therefore, that the number of organized corpuscles that are fixed by this method to the cotton filaments is quite significant compared to the volume of air (1); undoubtedly, it is not sufficient, to justify this generally accepted assertion, that the smallest bubble of ordinary air is capable of giving rise in an infusion to all the species of infusoria and all the Cryptogams specific to that infusion. But we will see in a subsequent chapter that this opinion is greatly exaggerated, and that one can always bring a considerable volume of ordinary air into contact with an infusion that has been brought to a boil, without the slightest organized growth occurring.
Footnote: (1) I hardly need to mention that I made sure that the cotton wool I used contained no organized particles whatsoever, and that its dissolution in the alcoholic mixture left no residue other than a few undissolved fibers. I should also point out that, at a thickness of one centimeter, a cotton wool is far from stopping all the particles in the air. If several layers of cotton wool are placed one after the other, the second, the third, and so on, become covered with dust; however, the further apart they are, the longer it takes to cover them to the same degree as the first.
I will now go into some detail so that you may have a clearer idea of the number of organized particles that are found in the dust collected as I have just described.
Figures 2, 3, and 4 of Plate II represent some organized particles from a dust sample collected over twenty-four hours, from November 16 to 17, 1859. Here is how these quick sketches, which show only the volume and outline of the particles, were made:
After washing the dust as I described earlier, I took a portion of the dust in a watch glass and dissolved it in a drop of potassium hydroxide solution, containing 5 parts potassium hydroxide to 100 parts water. As I moved the glass slide under the objective lens and observed an obviously organized globule, I drew it. This is how Figure 2 was obtained. The same procedure was followed for the others.
I then replaced the potassium hydroxide with aqueous iodine tincture. To do this, simply place a small square of blotting paper [aka bibulous paper, a type of strongly liquid-absorbing paper] against the edge of the glass slide, cover it with a second, then a third similar piece of paper, and so on until all the potassium hydroxide solution is absorbed. Replace it with a drop of iodine solution, which is removed in the same way to make way for a new drop of tincture. Continue in this way until the potassium hydroxide remaining under the glass slide is completely neutralized.
Fig. 3 shows some of the globules in contact with the aqueous iodine tincture. Finally, Fig. 4 shows the diagram of the globules examined after the iodine solution was replaced with ordinary sulfuric acid. The distance between the two parallels in Fig. 5 represents 1/100 of a millimeter at the magnification used in the experiment.
I should add that it took me an hour and a half to draw the diagrams of the globules and to perform the experiments substituting reagents for one another. This will give the reader a first indication of the number of organized corpuscles that can be stopped in twenty-four hours by passing approximately 1500 liters of air, taken from a quiet street in Paris, over a small cotton wad at a distance of 3 to 4 meters above the ground.
A much more accurate idea of the number of corpuscles that their shape and volume allow us to call organized can be obtained by determining the average number of these corpuscles contained within the field of view of the microscope, and by knowing the ratio of the surface area of the droplet spread under the small glass slide covering it to the field of view of the microscope, for the magnification used. The total number of corpuscles in the droplet will be equal to the ratio we are discussing, multiplied by the average number of corpuscles contained within any given field of view. We can thus recognize that a small cotton wad exposed for twenty-four hours to the air current of the street, taken a few meters above the ground, during the summer, after a succession of fine days, gathers several thousand organized corpuscles for an intake of approximately one liter of air per minute.
Moreover, this result varies infinitely with the state of the atmosphere, whether the experiment is conducted before or after rain, in calm or turbulent weather, during the day or at night, at a short or long distance from the ground. Finally, if we imagine all the countless causes that can increase or decrease the number of these solid particles that everyone has observed in a ray of sunlight entering a darkened room, we will understand the extent of the changes in the preceding results.
The method I have just described for collecting dust particles suspended in ordinary air and then examining them under a microscope is clearly capable of being usefully modified. I believe there would be great value in multiplying studies on this subject and comparing, in the same location with different seasons, and in different locations at the same time of year, the organized particles dispersed in the atmosphere. It seems that the phenomena of disease contagion, especially during periods of epidemic illness, would benefit from research pursued in this direction.
Figs. 6, 7, 8, and 9 of Plate II represent organized particles associated with amorphous particles, as they appear under a microscope at a magnification of 350 diameters; the diluting liquid was ordinary sulfuric acid. Figure 6 applies to dust collected from June 25 to 26, 1860; Figure 7 to dust from the very intense fog of February 1861; Figure 8 to dust collected from December 17 to 19, 1859, in temperatures ranging from -9 to -14°C; and finally, Figure 9 to dust from a layer of cotton that was preceded by another, in order to show that a first layer of cotton does not stop all the dust suspended in the air. However, it should be noted that the dust particles were very few in number here, and that it was necessary to change fields several times to observe an organized particle, whereas in ordinary cases, there is most often one or more organized particles in any given field.
CHAPTER 3: Experiments with heated air.
We have just seen that there are always organized corpuscles suspended in air, which, by their form, volume, and structure, cannot be distinguished from the germs of lower organisms, and their number is large without being excessive. Are there really fertile germs among them (1)? That is the truly interesting question; I believe I have succeeded in demonstrating it definitively. But before presenting the experiments that relate more specifically to this part of the subject, it is essential to first investigate whether the facts announced by Dr. Schwann concerning the inactivity of air that has been heated are accurate. Messrs. Pouchet, Mantegazza, Joly, and Musset dispute them. Let us try to see where the truth lies; this will also be the basis of our subsequent investigations.
Footnote: (1) The best and most direct course of action would be to follow the development of these germs under a microscope. This was my plan; but the apparatus I had built for this purpose was not delivered in a timely manner, and I was diverted from this study by other work. Moreover, one must not underestimate the difficulty of this method of observation. Nothing is simpler than to deposit the spores of a Mucedinaceae in a liquid suitable for nourishing them, to collect a few the next day or the day after, and to see that several have germinated and have already grown long appendages. But it is quite another thing to work on a single spore, which must then be located under the microscope in a specific position, while providing it with water to replace that which evaporates on the edges of the glass slide, etc. Then the very small Infusoria, Bacteria and Monads, quickly appear, take up the air, and the spore, deprived of one of its essential nutrients, does not develop. I hope to return to this part of my work soon.
In a 200 to 300 cubic centimeter flask, I introduce 100 to 150 cubic centimeters of an albuminous sugar solution, prepared in the following proportions:
Water: 100
Sugar: 10
Albuminoid and mineral matter from brewer's yeast [yeast extract]: 0.2 to 0.7.
[This type of solution will be referred to as “sugar yeast water”.]
[Yeast extract is produced as follows: yeast is boiled, and the resulting boiled yeast is then filtered to separate the water and dissolved substances from the non-dissolved solid substances. The dissolved substances are basically the nutrients which were inside the yeast cells before the boiling. If the water is then evaporated, the dissolved substances will remain as a powder, called yeast extract.]
The tapered neck of the flask connects to a platinum tube heated red-hot, as shown in Fig. 10, Plate I. The liquid is boiled for two to three minutes, then allowed to cool completely. It is filled with ordinary air at atmospheric pressure, all parts of which have been heated to red-hot temperature; then the neck of the flask is sealed [by melting the glass] with a flame, giving it the shape shown in Fig. 11.
The flask thus prepared is placed in an oven at a constant temperature of approximately 30°C. It can be kept there indefinitely without the liquid it contains undergoing the slightest alteration. Its clarity, its odor, and its very low acidity, barely perceptible on blue litmus paper, persist without appreciable change. Its color darkens slightly over time, undoubtedly under the influence of direct oxidation of the albuminoid matter or the sugar.
I affirm with the utmost sincerity that I have never had a single experiment, conducted as I have just described, that yielded a questionable result. Sugar yeast water, brought to a boil for two or three minutes and then exposed to air previously heated to red-hot temperature, does not deteriorate at all (1), even after eighteen months at a temperature of 25° to 30°C. However, if left in ordinary air, after a day or two it is clearly deteriorating and becomes filled with bacteria, vibrios, or covered with mucors.
Footnote: (1) I have certainly had occasion to repeat this experiment more than fifty times, and in no case has this highly perishable liquid shown any trace of organized growth in the presence of heated air.
Dr. Schwann's experiment applied to sugar yeast water is therefore irreproachably accurate. How is it, however, that several observers—Messrs. Pouchet, Mantegazza, and Schwann himself—arrived at contradictory results? I would add that Dr. Schwann himself was not always successful in his experiments on the inactivity of heated air; indeed, we saw in the first part of this Memoir, where I summarized this scientist's work, that his experiments on alcoholic fermentation often yielded results contrary to those he expected, without him being able to identify the presumed causes of error in these results.
In my own unpublished experiments, I had reached the conclusion that experiments conducted with heated air were only exceptionally successful. I will now recount some of them.
On August 9, 1857, I prepared several quarter-liter flasks as follows. In each of them, I placed 80 cubic centimeters of very clear sugar yeast water, containing per liter 100 grams of sugar and 3 grams of nitrogenous and mineral matter derived from the soluble components of the yeast. I drew the necks of the flasks open with a lamp, then brought the liquid to a boil, and then sealed the tapered end with a flame while the boiling process was maintained for two to four minutes. I then successively invert each flask into the mercury bath, breaking off their tips at the bottom.
Then, I introduce into the first flask approximately 70 cubic centimeters of oxygen prepared with potassium chloride, and passed through a porcelain tube heated red-hot before entering the flask. Into the second flask, I introduce 50 cubic centimeters of oxygen produced by the decomposition of water in a battery, and of very recent origin. Into the third and fourth flasks, I pass 50 to 60 cubic centimeters of ordinary air from a red-hot porcelain tube. Finally, into a fifth flask, I introduce 50 cubic centimeters of unheated ordinary air. I then place the five flasks in an oven at a constant temperature of 25 to 30°C, inverted over the mercury in stemmed glasses.
On August 13th, there are organized productions in the flasks. The liquid in the first flask was cloudy and milky due to the presence of a Torulaceae fungus in very fine granules arranged in strings. The second flask fell during the night of August 15th to 16th because it filled with gas through fermentation. Microscopic examination of the remaining liquid particles in the glass revealed globules of brewer's yeast. Flasks 3, 4, and 5 contained clumps of mold floating in a clear liquid.
In summary, I obtained results directly contrary to those of Dr. Schwann. Mucetidae and Torulaceae could develop in the presence of heated air, in liquids that had been boiled. I did not publish these experiments; the consequences that could be deduced from them were too serious for me not to fear some hidden source of error, despite the care I had taken to make them irreproachable. Indeed, I later succeeded in identifying this source of error.
In any case, things were such at that time that an observer, in good faith, repeating the experiments of Needham, Spallanzani, and Appert in the mercury bath, with the modification indicated by Dr. Schwann, arrived at conclusions entirely favorable to the doctrine of spontaneous generation, without it being possible to identify the true source of error in his experiments. One could only believe that it was very difficult to prevent a small amount of ordinary air from entering the vessels. But, besides the fact that this fear was exaggerated, we will see later that this was not at all the source of the method's inaccuracy.
In all these experiments, as in those of Dr. Schwann that had contradicted the results of his first experiment on meat broth, it was the mercury that had introduced the germs into the liquids. I will provide convincing proof of this later [in chapter 7]. But we can already observe that the mercury in a laboratory tank is constantly exposed to dust from the air, and that this liquid must therefore contain a multitude of these organized corpuscles, which we learned to study in the previous chapter. Their specific lightness would only be sufficient to bring them to the surface if they had a significant volume.
Moreover, even if these corpuscles were only present on the surface of the mercury, it would not be possible to avoid them during manipulations. Indeed, if one were to deposit dust on the mercury and then insert a glass tube, a test tube, or any other vessel, one would see the surface dust gradually enter the sheath that the solid object leaves between itself and the mercury. If the object is submerged to a depth of one decimeter or more, the dust will follow it to that depth, and [I wasn’t able to make sense of the remaining part of this sentence].
We can summarize the experiments in this chapter as follows. Sugar yeast water, a liquid that spoils extremely easily in contact with ordinary air, can be preserved intact for years when exposed to the action of heated air, after being boiled for two or three minutes. But the experiment must be carried out properly. Performed on the mercury bath with all imaginable care, it succeeds only exceptionally, if at all. The liquid spoils almost as easily as in ordinary air, because it is impossible for the handling, however directed, not to introduce germs from the inside or surface of the mercury or the walls of the bath.
The failure of experiments with heated air, whenever they were performed on the mercury bath, was not the only cause of uncertainty and confusion in this serious question of the generation of the lowest beings. If, in the preceding experiments, the sugar yeast water is replaced by milk, or some other liquid that we will come to know, and in whatever manner the experiment is conducted (whether one operates on the mercury bath, or whether one operates with the apparatus already described, represented in Fig. 10, and which gives such consistent results for sugar yeast water), the milk putrefies and shows organisms.
These diverse, seemingly contradictory results will find their natural explanation in one of the following chapters. But until then, they have been quite enough to sow confusion, as I have already tried to show in the historical chapter at the beginning of this work.
CHAPTER 4: Sowing of dust that exists in suspension in the air, in liquors which permit the development of lower organisms.
The results of the experiments in the two preceding chapters have taught us:
1. That there are always, suspended in ordinary air, organized particles quite similar to the germs of lower organisms.
2. That sugar yeast water, a liquid eminently susceptible to spoilage in ordinary air, remains intact and clear, without ever giving rise to infusoria or molds, when left in contact with air that has been previously heated.
Having established this, let us try to determine what would happen upon contact with this same air, by inoculating this sugary, albuminous water with the dust particles that we learned to collect in Chapter II, without introducing anything other than these particles. Whatever the experimental method, it must be done completely away from the mercury bath, because all the results would be skewed. I have directly observed this point of the question through specific experiments that I believe are of little use to recount here. I will, moreover, have occasion to return to the drawbacks of using mercury in these kinds of experiments.
Here are the arrangements I have adopted for depositing dust particles from the air into putrescible or fermentable liquids, in the presence of heated air. Let us return to our flask containing sugar yeast water and heated air, Fig. 11, Pl. 1. I will assume that the flask has been in an oven at 25° or 30° for one or two months, without having experienced any noticeable alteration, clear proof of the inactivity of the heated air with which it was filled under ordinary atmospheric pressure.
With the tip of the flask still closed, I adapt it, by means of a rubber tube, to an apparatus arranged as follows, Fig. 12: "T" is a strong glass tube, 10 to 12 millimeters in internal diameter, into which I have placed a short length of small-diameter tube, open at its ends, free to slide inside the larger tube and containing a portion of one of the small cotton wads laden with dust; "R" is a T-shaped brass tube, fitted with valves, one of these valves communicating with a pneumatic machine, another with a platinum tube heated to red-hot, and the third with tube "T"; "cc" represents the rubber that connects flask "B" to tube "T".
When all the parts of the apparatus are in place and the platinum tube is heated to red-hot by the gas heater shown in "G", a vacuum is created [by the “pneumatic machine”] after closing the valve that leads to the platinum tube. This valve is then opened [after closing the valve to the pneumatic machine] to allow heated air to gradually enter the apparatus. The vacuum and the re-entry of the heated air are repeated alternately ten to twelve times. The nitrocellulose is thus filled with heated air down to the smallest interstices of the fibers, but it retains its dust.
[Remember that Pasteur is trying to prove that it is the airborne dust particles resembling germs, and not any other component of air, which are responsible for fermentation. Therefore he wants to flush all the old, unheated air out of the piece of nitrocellulose. He does this by exposing the nitrocellulose to air which has been heated, then sucking the air out, and then repeating this many times to be sure that all the old air has been removed from the fibers. Then, only dust particles and air which has been heated remain in the fibers... Or at least that’s the idea. I don’t know if it is actually possible to replace every molecule of air from a piece of nitrocellulose in this way, but I believe it is not. Therefore I don’t think this experiment is 100% convincing, though it is still a very clever experiment.]
This done, I break the tip of the flask "B" through the [rubber] water-clamp "cc", without untying the cords, then I pour the small dust tube into the flask. Finally, I close the neck of the flask with a flame, and it is returned to the oven. Now, it consistently happens that products begins to appear in the flask after twenty-four, thirty-six, or forty-eight hours at most. This is precisely the time required for these same products to appear in the sugar yeast water when it is exposed to contact with ordinary air.
Here are the details of some experiments: In the first days of November 1859, I prepared, according to the method shown in Fig. 10, several flasks with a capacity of 250 cubic centimeters, containing 100 cubic centimeters of sugar yeast water and 150 cubic centimeters of heated air. They remained in the oven at a temperature close to 30°C until January 8, 1860. On that day, around nine o'clock in the morning, I introduced into one of these flasks, using the apparatus shown in Fig. 12, a portion of cotton laden with dust, collected as explained in Chapter II.
On January 9 at nine o'clock in the morning, the liquid in the flask showed nothing unusual. The same day, at six o'clock in the evening, small tufts of mold could be clearly seen emerging from the dust tube. The liquid was perfectly clear. On January 10th, at five o'clock in the evening, in addition to the silky clumps of mold, the liquid, which had always remained perfectly clear, I noticed on the walls of the flask a large number of white streaks, iridescent with various colors when the flask was held up to the light. On January 11th, the liquid had lost its clarity. It was completely cloudy, to the point that the clumps of mycelium were no longer visible. Then I opened the flask with a file and studied under the microscope the various growths that had developed within it.
The cloudiness of the liquid is due to a multitude of tiny bacteria, very rapid in their movements, pirouetting briskly or swaying, etc., Fig. 13, Pl. II. The silky tufts are formed by a mycelium in branching tubes, Fig. 14. Finally, this kind of powdery precipitate in the form of white streaks, which appeared on January 10, is composed of a very elegant Torulaceae, shown in Fig. 15. This is a very common Torulaceae in sweet, albuminous liquids, which develops, for example, in slightly acidified beet juice, in the urine of diabetics, and which could be confused with brewer's yeast, to which it closely resembles in its mode of development, were it not for the fact that the diameter of its globules is significantly smaller than that of yeast cells, smaller by a third or even half. The globules of this Torulaceae are less granular, more translucent than the globules of brewer's yeast. The nucleus, when visible, is single and very distinct. These globules multiply by budding and take on the branched form of brewer's yeast during multiplication.
Thus, here are three products arising under the influence of the dust that was sown, products of the same kind as those seen arising in these same sugary, albuminous liquids when left in contact with ordinary air.
On January 17th, I introduced dust into two other flasks of sugar yeast water that had remained unaltered since November. On the morning of the 19th, one of the liquids was completely cloudy. Moreover, it showed no sign of mycelium. The liquid in the other flask was still very clear. No sign of organized growth. The same day at five o'clock in the evening, the first flask was in the same state; the cloudiness was only increased. As for the other, the clarity of its liquid was still perfect, but a clump of mycelium emerged from the small dust tube and covered one end of it.
On the 20th, the condition of the first flask had not changed significantly. The mold in the second flask had grown considerably, and a new mold had formed within the liquid. Furthermore, the liquid's clarity appeared slightly altered. On the 21st, the liquid in the second flask was almost as cloudy as that of the first, and the mycelium clumps had not grown at all since the previous day, that is, since the cloudiness had become apparent throughout the liquid. On January 22nd and 23rd, the mycelium clumps remained unchanged, and there is no doubt, as we shall see, that the cessation of their development must be attributed to the presence of the Infusoria, which cloud the liquid and, by consuming the dissolved oxygen, deprive the plant [mold] of one of its most essential nutrients. [Pasteur refers to the mold as a plant. In modern biology, mold and yeast are no longer classified as plants, but as fungi.] This result is consistent, and this explains why, in the first flask, the initial growth was formed by Infusoria, and no other organized growth was observed.
Here is a remarkable confirmation of this opinion: On January 23, seeing that the clumps of mycelium in the second flask had remained stationary since the 20th, I dropped the small dust tube into the neck of the flask, as shown in Fig. 16, Pl. I, in order to expose the clump of mold covering one end of this small tube to the atmosphere of the flask, and thus eliminate the influence of the Infusoria. Now, eighteen hours later, as early as the morning of January 24, the mold had sent out filaments in all directions, which covered the small lobe and the neck of the flask. On the 25th, it fruited. On the 27th, it partially spread to the surface of the liquid in the flask. From that day on, it did not grow any larger and remained completely stationary, because all the oxygen in the air of the flask had disappeared and had been replaced by carbonic acid.
These facts, which I have often observed in similar circumstances, demonstrate the significant influence that simultaneously developing organisms can have on one another, how they can harm each other, and how it can happen that a liquid may contain a variety of organisms, though far fewer in number in each particular case than the sown germs, and that no more could develop under any circumstances. Those that are multiplying first smother the others.
All those who have studied the organized production of infusions have noted that an infusion is more or less completely devoid of infusoria if it happens to become covered with molds in the first few days of its exposure to air. Conversely, when it begins with infusoria, it hardly shows any mold. The cause of this is similar to the one I just described. In the first case, oxygen is absorbed by the Mucedinea, in the second by the Infusoria. What I say about oxygen can undoubtedly be applied to the other foods of these small creatures.
I have illustrated, Fig. 17, Pl. II, the Mucedinea that developed in the neck of the flask, which was opened on January 31st, in order to study the organisms it produced. At the bottom of the liquid, which had cleared over several days because the mold had in turn hindered the development of the Infusoria, there was a noticeable, yellowish-white deposit composed solely of the corpses of small Bacteria and Vibrio bacteria. All of them, without exception, showed no movement other than Brownian motion.
As for the Mucedinea, its mycelium had grown vertical, translucent, colorless, unbranched tubes, bearing at their tips small balls colored dark brown in the older individuals. These sporangia are easily crushed under a glass slide, revealing spores inside. It is then very clearly recognized that these sporangia have a membranous envelope, because this ruptures under pressure. If a drop of water is then placed under the glass slide, the small sphere instantly empties, and clusters of ovoid spores, perfectly translucent and with very sharp outlines, emerge in rapid streams. Their diameter varies from 0.006 to 0.008 millimeters. These are all the characteristics of the most common species of the genus Ascophora.
But in addition, besides this Mucedinaceae, I encountered a very different one belonging to the genus Penicillium, shown in Fig. 18; and within the small dust tube itself, mixed with the cotton fibers, was a Torula in large cells of 0.02 to 0.04 mm in diameter, joined to much longer segments resulting from the development of these generally very granular cells. It is shown in Fig. 19.
I could multiply many examples of growths occurring in sugar yeast water due to the seeding of airborne dust particles within an atmosphere of air that has been pre-heated and is itself completely inactive. I have chosen to describe them primarily through experiments that showed me very common organized growths, which frequently appear in liquids of the type I was using. Mucorea, Torulaceae, and the most diverse Mucedinaceae species originate. As for Infusoria, in this type of liquid, they are always small Bacteria, the smallest Monads, or the smallest Vibrios.
Now, all these growths are precisely of the type seen to appear in the liquid in question when it is freely exposed to ordinary air. As for Infusoria, I can affirm that I have never, under any circumstances, seen sugar yeast water give rise to Infusoria other than Bacteria and the smallest Vibrio species. The largest Infusoria I have encountered is Monas lens, 0.004 mm in diameter, and even then I have seen it only very rarely, either in open air or in closed flasks. As for the plants, they are Mucors, common Mucedinaceae, or Torulaceae (1).
Footnote: (1) I must state here, once and for all, that I call Mucor those organized plant growths that develop preferentially on the surface of liquids, and which have a more or less oily or gelatinous appearance, with thin or thick, moist or dry, and sometimes wrinkled film; Mucedinaceae, the molds proper whose mycelium is formed of variously branched tubes, and which offer on the surface of the liquid fruiting bodies usually colored in the form of dust, and sometimes of tubes visible to the naked eye, ending in sporangia as in the most common molds; and finally Torulaceae the small non-tubular cellular plants, which appear at the bottom of the liquid where they multiply by budding, taking the form of precipitates, in the manner of brewer's yeast.
One might perhaps wonder whether, in the preceding experiments, cotton, as an organic material, had any influence on the results. It is especially important to know what would happen if the manipulations were repeated on flasks prepared as described, and with the dust removed from the air. In other words, does the manipulation required for introducing the dust have no influence in itself? It is essential to ascertain this.
To answer these questions, I replaced the cotton with asbestos. The asbestos wadding, after exposure for a few hours to the airflow from the aspirator (Fig. 1), was introduced into the flasks following the preceding instructions, and it produced results entirely similar to those we have just reported.
But with asbestos wads that had been previously heated and were not laden with dust, or with asbestos laden with dust but subsequently heated, no cloudiness, infusoria, or plants of any kind appeared. The liquids remained perfectly clear. I repeated these comparative experiments a great many times, and I was always surprised by their clarity and perfect consistency. It would seem, in fact, that experiments of this delicacy should sometimes offer contradictory results brought about by accidental causes of error. Yet, I have never once seen the blank experiments succeed, just as I have never seen the inoculation of dust fail to produce organized growth.
[I think nitrocellulose cannot be heated because it is explosive, which is the reason why Pasteur switches to using asbestos as a filter.]
In the presence of such results, confirmed and expanded by those of the following chapters, I consider it mathematically demonstrated that all organized productions, which form in ordinary air in sugary albuminous water, previously brought to a boil, originate from the solid particles that are suspended in the air.
But, on the other hand, we saw in Chapter 2 that these solid particles contain, amidst a multitude of amorphous debris—calcium carbonate, silica, soot, strands of wool, etc.—organized corpuscles that closely resemble the tiny seeds of the products whose formation we observed in this liquid. These corpuscles are therefore the fertile germs of these products.
Let us conclude, moreover, that if heated air placed in the presence of an Appert preserve made from albuminous sugar water, such as grape must, does not spoil, as Dr. Schwann was the first to discover, it is because the heat has destroyed the germs carried by this air. This is what all the opponents of heterogenesis predicted. I have merely provided solid and decisive proofs, compelling unbiased minds to reject any notion of the existence in the air of a more or less mysterious principle—gas, fluid, ozone, etc.—capable of causing any kind of organization in infusions.
There is a very interesting question to address here, which I will return to in a separate publication, and which will undoubtedly surprise the reader. Nothing is more conducive to alcoholic fermentation than the liquid studied in the preceding pages. Sugar yeast water is composed in the same way as grape must, beer wort, beet juice, etc., liquids which, when exposed to ordinary air, readily undergo fermentation. However, in a considerable number of experiments set up as I described earlier, and in which I dispersed airborne particles into sugar yeast water, I never managed to obtain fermentation of the sugary liquid (1).
Footnote: (1) I will show later that this peculiarity stems from the relation that existed in my experiments between the volumes of air and liquid.
It is important to point out here that nothing could be further from the truth than this assertion, often repeated by proponents of the doctrine of spontaneous generation, "that the appearance of the first organisms is always preceded by phenomena of fermentation or putrefaction, and that the formation of animalcules in macerations follows the release of various gases due to the decomposition of the substances used, and that it is after the manifestation of these phenomena that a particular film forms on the surface of the liquids (1)."
Footnote: (1) Pouchet, Traité de la génération spontanée, 1859, pp. 352 and 353.
Therefore, when people speak to me of fermentable movement, which I create in my liquids by scattering dust particles, "fermentable movement necessary for the evolution of generative forces," I see only vague words, to which experience teaches me not to ascribe any reasonable meaning.
CHAPTER 5: Extension of the previous results to new, highly deteriorable liquids. –Urine. –Milk. –Sugar albuminous water mixed with calcium carbonate.
§ 1 – Urine.
It is well known how easily fresh urine deteriorates upon contact with atmospheric air. Most commonly, it loses its acidity, becomes cloudy, gives off a strong ammoniacal odor, and deposits crystals of various kinds. Careful microscopic examination reveals that the cloudiness of the liquid, the deposit that forms at the bottom of the container, and the film that often gradually covers the entire surface of the liquid, are composed of organized productions.
The most frequent are as follows: the film on the surface of the liquid is often a mucoid membrane, formed of extremely fine granules or, more accurately, segments; they resemble motionless clusters of Bacterium termo. This seems all the more probable since, within this same film, are very small monads moving rapidly in circular motion. This membranous film falls, in whole or in part, to the bottom of the vessel as soon as it becomes heavy enough in certain areas, then a new one forms, which in turn falls away—hence the origin of certain deposits in urine undergoing deterioration.
At other times, islets of Mucetaceae, especially Penicillium glaucum, develop on the surface of the urine, although they spread only with difficulty and do not acquire their characteristic bluish-green color.
Finally, when the ambient temperature does not rise above 15°C, the urine quite frequently becomes covered with a continuous film, difficult to tear, which reforms immediately without interruption as soon as the glass rod used to try to separate its parts is removed. When this film forms, the urine often remains acidic and does not become noticeably cloudy. This film is formed by a remarkable Mucorea, very similar to Torulaceae (Fig. 15, Pl. II), but which I nevertheless believe to be specifically distinct. It is shown in Fig. 20. These are translucent cells where the nucleus is rarely visible, multiplying by budding. The diameter of the cells varies from 0.0045 mm to 0.0065 mm, significantly smaller than that of brewer's yeast globules.
As for the deposit that forms at the bottom and on the sides of a vessel of urine exposed to air, it contains, in addition to the products that have fallen from the surface, crystals of varying nature. But what I particularly want to emphasize is the presence of a Torulaceae in chains of very small grains, Fig. 21, whenever the liquid has become ammoniacal through the transformation of urea. I am strongly inclined to believe that this production constitutes an organized ferment, and that there is never a transformation of urea into ammonium carbonate without the presence and development of this small plant. However, as my experiments on this point are not yet complete, I must express some reservations in my opinion.
What I can affirm in all cases is the inaccuracy of a fact that has often been cited in discussions concerning theories about the origin of fermentation. This well-known fact supposedly consists of the decomposition of urea under the influence of the alcoholic fermentation of sugar. Every time I have seen the experiment succeed, the brewer's yeast has been found mixed with the Torulaceae in the stringy form I just mentioned, and when the brewer's yeast remained homogeneous, without mixing with any other particular product, the urea had undergone no alteration. The preceding fact, when better studied, therefore agrees with the new ideas I have put forward in recent years concerning the origin of fermentations proper.
We have just identified the most ordinary products of urine exposed to contact with air, which appear simultaneously or separately. Let us now examine what happens when urine is subjected to the action of heated air. For this, let us return to the apparatus of Fig. 10, Plate 1. Fresh, filtered urine is boiled for two to three minutes in the flask, which is connected to the red-hot platinum tube. The boiling is then stopped so that the flask, having cooled, is filled with heated air under pressure and at ordinary temperature; it is then sealed with a flame at the base of the tapered neck.
The flask, as shown in Fig. 2, is then placed in an oven at a temperature of 25 to 30°C, a temperature so favorable to the putrefaction of urine. It can stay there indefinitely, without experiencing any alteration other than a slow oxidation of the albuminous matter of the urine; at least the urine darkens a little in color over time, and analysis of the air in the flask shows a loss of oxygen and a gain of carbonic acid.
On April 14, 1860, I analyzed the air in a flask prepared as I have just described, which had been in an oven since February 18 of the same year. The air then contained:
Oxygen: 19.3
Carbonic acid: 3.9
Nitrogen by difference: 76.8
[Total] 100.0
But the clarity of the urine remains perfect, even after eighteen months, and not the slightest animal or vegetable production appears; it also retains its original acidity and odor. The urine, which has been brought to boiling point, therefore undergoes no putrefaction or fermentation in the presence of heated air (1). Let us now see what happens to this liquid when all the preceding conditions are met, and when the dust particles suspended in the air are deposited into it.
Long Footnote: (1) But it will not be useless to point out here that this experiment, carried out with the aid of the mercury bath, gives positive results, without the introduction, seemingly, of anything that could contain germs. If we take, for example, the flask from Fig. 11, and break its tip at the bottom of the mercury bath, then release some gas so that the mercury can then return to the flask, it will happen at least nine times out of ten, if not always, that molds or small infusoria will appear in the liquid. It is the mercury that introduces the germs.
I will report only one experiment of this kind. The flask mentioned in the text was returned to the oven on April 14th, after the volume of air necessary for the analysis had been taken from the mercury bath. This flask was inverted in a stemmed glass over the mercury. Now, here is what happened: on April 16th, at the bottom of the urine, at the interface between the urine and the mercury, there were twelve small tufts of mycelium. The liquid remained perfectly clear, proof of the absolute absence of Infusoria. On April 21st, several of the small tufts, joined together by juxtaposition, had grown so much that they reached the surface of the urine, and their tubes were thus in contact with the air. The liquid remained perfectly clear. By the evening of April 21st, an island had formed on the surface of the liquid, with visible sporangia, green in color and entirely reminiscent of Penicillium glaucum. A few days later, the Mucedinea occupied more than half of the liquid's surface.
I then analyzed the gas in the flask again. It contained:
Carbonic acid: 19.5
Oxygen: 0.0
Nitrogen by difference: 80.5
[Total] 100.0
It is worth noting that, according to this analysis, a Mucedinaceae plant depletes even the smallest quantities of free oxygen in the air of a sealed flask through its vegetation.
End footnote.
On March 16, 1860, I introduced a small wad of asbestos, which had been exposed for a few hours to a normal air current, into a flask containing urine and heated air. The introduction of the asbestos dust was carried out following the method in Fig. 12, with all the precautions already indicated in the previous chapter. On March 17, there was no cloudiness, no mold, and no Torulaceae. No crystals were deposited.
On the 18th, there was no apparent mold, either in the tube or elsewhere, but the liquid was cloudy, as always happens when infusoria develop. As I have observed, it is the very movement of these tiny organisms that causes the liquid to become cloudy. [According to what I’ve read, it is the presence of cell material, and not the movement of the cells, which causes light scattering and thus cloudiness in liquid.] As soon as they die from lack of air, they gather at the bottom of the vessel, like a precipitate, and the liquid clears. On March 19th, the cloudiness still existed and had already formed a very noticeable deposit at the bottom of the flask, a white, slightly viscous deposit.
On March 20th and 21st, the situation remained unchanged. On the evening of the 21st, many small crystals were deposited on the surface of the liquid and coated all the walls of the flask. This deposit of crystals indicates that the liquid must be ammoniacal and that it has deteriorated according to one of the ordinary modes of putrefaction of urine, upon contact with ordinary air.
On March 23rd, I opened the flask in the mercury. There was no pressure indicating the release of gas. The liquid was very noticeably alkaline on red litmus paper; however, the alkaline reaction, as well as the action of hydrochloric acid, indicated that not much ammonium carbonate had yet formed. Microscopic examination revealed the formation of three types of crystals, a multitude of small bacteria, several of which were still very agile, and very small monads moving along curves. There was also Torulaceae (Fig. 21, Pl. II) in small grains arranged in short chains. The result of this microscopic examination is shown in Fig. 22; only the crystals and organized structures are shown separately.
The diameter of the Torulaceae grains in these small chains was approximately 0.0015 mm. This is the organized ferment that I consider to be the urine ferment, that is, the one that causes the transformation of urea into ammonium carbonate, and which, subsequently, due to the resulting alkalinity, leads to the deposition of alkali urates and magnesium ammonium phosphate. Urine, left to itself and remaining acidic, does allow crystals to be deposited, but these are uric acid crystals. I have drawn, fig. 23, crystals of this acid, deposited in urine that had remained acidic for fifteen days, at a temperature of 11°C, and on the surface of which only the Mucorea already represented fig. 20 had formed.
I could multiply the examples of the reactions of urine in the presence of heated air, under the influence of dust particles found in ordinary air, but this would be of little use: Bacteria, Monads, Mucedins, various Torulacea—these are always what is observed. However, Mucedins are generally less frequent than in experiments with albuminous sugar water. What must be noted above all is that there is no more variety in the products offered by urine exposed to ordinary air than there is in those of urine exposed to heated air, under the influence of dust particles floating in air. The difference, if it exists, is rather in favor of the second method of experimentation.
Our conclusion, therefore, is that whenever urine deteriorates upon contact with ordinary air, it is due to the solid dust particles carried by the air that fall into the liquid. We can already observe, from the details of the experiments I have reported so far, how frequent the formation of the smallest infusoria is, and especially of Bacterium termo, which appears in all kinds of infusions and almost always before other infusoria. This infusoria is so small that one cannot distinguish its germ, much less determine its presence, even if it were known, among the organized particles of dust suspended in the air.
But how could it not exist in the air, given its abundance everywhere? I have no other proof than that which can be deduced from the microscopic examination of a multitude of putrefying substances. Let us also recall Leewenhoek's observations on the infusoria of the white matter that accumulates between the teeth, and which is present in everyone's mouth, regardless of the care taken to keep one's teeth as perfectly clean as possible. Bacteria swarm in the smallest particle of this matter. They are found in large quantities in the intestinal canal and in excrement.
§ 2 — Milk. — Sugary albuminous water with calcium carbonate.
The study of milk and some other liquids will offer us results that will at first appear singularly perplexing. When, in the preceding chapters, we dealt with sugar yeast water and urine, we observed that these liquids, brought to boiling point at 100°C for two or three minutes, and then exposed to air that has been heated to a red-hot temperature, undergo no alteration. The experiment, conducted as I described it using the apparatus shown in Fig. 10, Pl. I, never fails.
That being said, if this same experiment is repeated on ordinary milk, one can be certain that the milk will curdle and putrefy invariably. On April 10, 1860, I prepared a flask of milk with the apparatus shown in Fig. 10. The boiling lasted two minutes, from the moment the steam had sufficiently heated the tapered end of the neck so that it was impossible to hold a hand there. After the liquid had cooled, the neck of the flask was sealed with a flame as usual, and it was placed in an oven at a temperature of 25° to 30°C.
On April 17, the milk in this flask had curdled. There was no sign of gas being released. I removed the neck with a file. There was a faint odor of curdled milk. The whey was as alkaline as fresh milk. Examined under the microscope, I found it filled with Vibrio bacteria of the same species, but of highly variable lengths. They had a slow, sinuous movement; there was no Bacterium termo at all, nor any other animal or vegetable matter. It is therefore beyond doubt that the milk curdled under the influence of these Vibrio bacteria, perhaps through the production of a rennet-like liquid. Many of these Vibrio bacteria were up to 0.05 mm long; the smallest were 0.004 mm. Many were motionless.
Analysis of the air in the flask yielded the following:
Oxygen: 0.8
Carbonic acid: 17.2
Hydrogen: 0.2
Nitrogen by difference: 81.8
[Total] 100.0
This analysis shows that the oxygen had largely disappeared and had been replaced by carbonic acid, undoubtedly under the influence of Vibrio respiration. The fact that Vibrio were still alive when the flask was opened, even though there was less that 1/100 oxygen, demonstrates that the life of these tiny organisms continues as long as oxygen is present, even when the proportion of carbonic acid is considerable. We have already observed a similar phenomenon with the Mucetidae on page 54.
Although the milk in this flask took seven days to curdle, from April 10th to 17th, it should not be concluded that the phenomenon only manifested itself after seven days. If the flask had been opened on the 12th or the 13th, the presence of Infusoria and a very slight beginning of coagulation would have been evident. Coagulation generally occurs within three to ten days, but in one case, it only appeared after a month in the incubator, from March 11th to April 16th. This only indicates that the Infusoria multiplied laboriously and slowly.
The experiments we have just described have always yielded similar results. Milk boiled at 100°C and left in contact with heated air fills, after a few days, with small infusoria, most often a variety of Vibrio lineola (Fig. 24, Pl. II), and with bacteria, and, while retaining its alkalinity, it curdles.
I have never seen anything other than Vibrio and Bacterium form in milk treated in this way; no Mucedinaceae, no Torulaceae, no vegetable ferments. There is no doubt that this is due to the fact that the germs of these latter organisms cannot withstand 100°C in water, a fact I have also observed through direct experimentation. Similarly, we will recognize that if milk spoils under the preceding circumstances, it is because the infusoria we have just discussed can withstand the humid temperature of 100°C when the liquid in which they are heated possesses certain properties.
Regarding the coagulation of milk, we see from these experiments that milk left in contact with air curdles under two very different influences. It can curdle due to the development of infusoria, a phenomenon that probably falls under the category of milk coagulation by rennet. It is worth investigating whether, as a result of the life of the infusoria, a liquid similar to that produced by natural or artificial rennet is created, which can also produce coagulation without acidity.
On the other hand, there is the coagulation of milk under the influence of lactic acid. When fresh, unboiled milk is left in contact with air, coagulation is most often due to this second cause. As for the acidity itself, it is caused by the development of plant ferments, particularly the lactic ferment, which transform the milk sugar into lactic acid or other acids, ferments which cannot be born when the milk has been boiled, and is exposed to heated air, because the germs of these ferments do not resist 100°C.
I stated that the putrefaction of milk heated to 100°C and exposed to heated air was due to the fact that, in certain cases, Vibrio bacteria resist a temperature of 100°C. This is easily demonstrated. Let us return to the apparatus shown in Fig. 10, Pl. 1, and boil the milk at a temperature slightly above 100°C, 110°C at most, by attaching the glass tube from Fig. 10-bis [on the far-left side of plate I] to the left end of the platinum tube, immersing 40 to 50 cubic centimeters in the mercury of the long basin shown in that same figure. Let us detach this glass tube when the milk has boiled for only a minute or two; then let us close the neck of the flask with a flame, as we have always done.
[It seems to me that by allowing 50 cm^3 of mercury to enter the glass tube (Fig. 10-bis), the air inside the closed system is compressed by the mercury, and this air compression causes an increase in air pressure. At least, I cannot think of any other explanation of how the mercury can increase the air pressure.]
These prepared flasks can then remain indefinitely in the oven without ever giving rise to the slightest growth of mold or any kind of spoilage. The milk retains its flavor, its aroma, and all its qualities. It is surprising that its fat does not oxidize more rapidly in the presence of such a considerable volume of air. This oxidation does occur, however, but it is very slight. Here is the analysis of the air in a flask that had remained in the oven for forty days:
Oxygen: 18.37
Carbonic acid: 0.16
Nitrogen by difference: 81.47
[Total] 100.00
Under the influence of this direct oxidation, the cream curdles slightly and imparts a faint tallowy flavor to the milk. Thus, the putrefaction of milk boiled at 100°C and exposed to heated air was merely an accident caused by the fact that the boiling temperature had not been high enough. It suffices to boil it at 100-something degrees, or to prolong the boiling at 100°C, for the results to have all the clarity and precision of those we have already obtained by working with sugar yeast water and urine.
But, one might ask, how is it that sugar yeast water and urine only need to be boiled at 100°C for Vibrio bacteria to never appear in contact with heated air? We will acknowledge that this is likely due to the fact that these liquids are very weakly acidic, while milk is alkaline. Indeed, I have observed that Vibrio bacteria can be produced, using sugar yeast water, in contact with heated air. It suffices to boil the liquid at 100°C in the presence of a little calcium carbonate, which renders the liquid neutral or slightly alkaline.
On March 21, 1860, I prepared six flasks using the apparatus shown in Fig. 10; each of them contained:
10 grams of sugar.
100 centiliters of beer yeast water (0.5 g of solid matter).
1 gram of calcium carbonate.
After filling them with heated air, I sealed them with a flame and placed them in the oven. On March 25th, the liquid in these flasks was cloudy, and everything indicated that they contained Infusoria. The cloudiness had begun in three of them as early as March 23rd. I opened one of these flasks on March 25th, and indeed, I found the liquid filled with very small Vibrio, several of which were visibly moving, albeit very slowly—they were as if sick.
On April 5th, the [remaining] flasks that had not been opened showed on their surface a thick, wrinkled, reddish-colored, gelatinous Mucor. Under the microscope, this Mucor consists of a mass of extremely fine granules. At the bottom of the liquid is a deposit of dead small Vibrios. I believe that this Mucor is a cryptogamic plant species independent of Vibrio production, and that, consequently, the germ of this particular Mucor, as well as the Vibrio germ, has survived, under these particular conditions, a temperature of 100°C for two to three minutes.
If we now repeat these same tests, boiling the liquid at only 105°C, as we did earlier with the milk, we will see no cloudiness or mucorrhea whatsoever. Therefore, it is beyond doubt that if milk spoils in the presence of heated air when it has only been boiled at 100°C, it is because it is slightly alkaline, since adding a little chalk to sugar yeast water is enough to impart the same properties to it—properties it never possesses if boiled without the addition of chalk.
But let us continue these studies and see what happens in the presence of heated air when we sprinkle the dust from the air into milk preserved intact by boiling at 100-something degrees. On April 7, 1860, I placed a small amount of asbestos wadding, laden with airborne dust, into a flask containing milk boiled at 108°C that had remained unchanged for two months. On April 9 and 10, the milk appeared intact. But already on the evening of April 10, the creamy layer on the surface trapped gas bubbles. I agitated it to make them disappear; two hours later, new bubbles had already formed. On the 11th, fermentation continued to manifest itself through gas bubbles; but the milk had not curdled. On the 12th, the situation was the same as the day before.
On April 15, the milk, while not curdled, appeared clearer. I opened the flask in the mercury bath to examine its contents. A significant quantity of gas escaped forcefully from the flask; it was therefore certain that fermentation had occurred. However, the liquid is not acidic; it even still has a hint of alkalinity on red litmus paper. Its odor is faint, though noticeable and quite peculiar; it is the smell of sour milk, or more precisely, the smell of infants at the breast when they are poorly cared for [lol? original: “l’odeur des petits enfants à la mamelle lorsqu’ils sont mal soignés”]. The taste of the milk is sweet at first, then it soon gives way to another very unpleasant taste that has something bitter and peppery about it.
Exposed for a few moments to a water bath, the milk curdles immediately, producing a completely opaque whey. Under the microscope, one sees mixed with the butter [milk fat] globules a multitude of small objects, often constricted in the middle: this is the elongated variety of Bacterium termo, which was also mixed with the small Vibrio lineola. All are motionless. One also sees a multitude of objects with a diameter almost twice that of the bacterium, characterized by a kind of spherical head at one end. Their number is at least equal to that of Bacteria and Vibrions. Like them, they have no apparent movements.
Here is the gas analysis:
Oxygen: 2.3
Carbonic acid: 28.6
Hydrogen: 11.0
Nitrogen by difference: 58.1
[Total] 100.0
I repeated this experiment several times on milk or on sugar yeast water mixed with calcium carbonate; it always gave similar results, that is to say, I have never been able to scatter dust particles from the air into liquids preserved intact by the method I have indicated without seeing the appearance, after a very few days, of either Mucors or various Mucedinaceae, or Infusoria.
It follows that if milk boiled at 100-something degrees neither spoils nor curdles upon contact with heated air, it is not because it has lost this property, since it suffices to deposit dust collected from ordinary air on it to see it produce organized formations of the same kind as those that fresh milk shows after a few days when exposed to ordinary air.
Consequently, if it putrefies and displays infusoria upon contact with heated air when it has only been boiled at 100°C, it is evidently because the germs of these infusoria can withstand a temperature of 100°C for a few minutes. The following experiment will provide direct proof of this.
A flask of milk has been kept intact for two months in the presence of heated air. I deposited dust particles from the air onto it, following the method shown in Fig. 12, Pl. I, and described in Chapter IV. I immediately sealed the flask with a flame and placed it entirely in a pot of rapidly boiling water. I left it there for five minutes, then removed it to place it in an oven: this was July 24, 1860.
[The purpose of putting the flask in boiling water is to show that the bacterial germs in the dust, which were transferred to the flask, can withstand 100°C for a short time.]
On July 30, it visibly began to curdle; on the 31st, it was completely curdled. I then opened it to study the liquid under a microscope; I discovered a multitude of very agile Bacteria and Vibrios. On red litmus paper, the whey retained all its original alkalinity.
I would have liked to investigate the true origin of the Vibrio bacteria that appear in milk boiled at 100°C and then exposed to heated air. Do these bacteria exist in natural milk? It is possible. However, I am more inclined to believe that they simply belong to the dust that falls into the milk during and after milking, or that is always present in the vessels used to collect the milk.
I have encountered difficulties, which I have not yet resolved, in introducing natural milk, which had had no contact with ordinary air, into my flasks in the presence of heated air. I was able to properly carry out the experiment with urine, and I saw that this liquid remained completely unaltered upon contact with heated air, even though it had not undergone any temperature increase. Nevertheless, these are experiments that I intend to repeat and pursue with particular care. Everyone will understand its importance.
CHAPTER 6: Another simple method to demonstrate that all organized productions of infusions (previously heated) originate from the particles that exist in suspension in atmospheric air.
I believe I have rigorously established in the preceding chapters that all organized productions of infusions, once heated, have no other origin than the solid particles that the air constantly carries and deposits on all objects. If any doubt could still remain in the reader's mind on this point, it will be dispelled by the experiments I am about to describe.
I place one of the following liquids, all highly perishable upon contact with ordinary air, into a glass flask: yeast water, sugar yeast water, urine, beetroot juice, or pepper water. Then, using a flame, I stretch the neck of the flask to create various curves, as shown in Fig. 25, Pl. I.
I then bring the liquid to a boil for a few minutes until steam escapes abundantly from the open end of the tapered neck, without any other precautions. I then allow the flask to cool. A singular thing, quite likely to astonish anyone accustomed to the delicate nature of experiments concerning so-called spontaneous generation, is that the liquid in this flask will remain indefinitely unaltered. It can be handled without any fear, transported from one place to another, subjected to all the temperature variations of the seasons, and its liquid will not undergo the slightest alteration and will retain its odor and taste; it is an excellent Appert preserve.
There will be no other change in its nature than that which, in certain cases, can be brought about by a direct, purely chemical oxidation of the matter. But we have seen from the analyses I have presented in this Memoir how limited this action of oxygen is whenever there are no organized products developed in the liquids (1).
< Footnote: (1) I will demonstrate, in subsequent works, the importance of this last remark. I will show that many lower organisms have the property of transporting oxygen from the air, in considerable quantities, to complex organic matter, and that this is one of the means nature uses to transform the elements of organic substances, produced under the influence of life, into water, carbonic acid, carbon monoxide, nitrogen, nitric acid, and ammonia. For example, with the help of Mycoderms, enormous masses of alcohol or acetic acid can be reduced to water and carbonic acid; and through the relatively small development of any Mucedin, a very high weight of sugar, tartaric acid, citric acid, and albuminoid matter can be burned. End footnote >
It seems that ordinary air, entering forcefully at first [once the boiling has stopped], must arrive in the flask completely untreated. This is true, but it encounters a liquid still close to boiling point. The air then enters more slowly, and when the liquid is sufficiently cooled to no longer deprive the germs of their vitality, the air entry slows enough that it leaves behind in the moist curves of the neck all the dust capable of affecting the infusions and causing organized growth. At least, I see no other possible explanation for these curious experiments.
If, after one or more months of residence in the oven, the neck of the flask is removed by a cut with a file, without otherwise touching the flask (fig. 26, Pl. I), and after twenty-four, thirty-six or forty-eight hours, the molds and Infusoria will begin to show themselves absolutely as usual, or as if dust from the air had been sown in the flask, according to the method of fig. 12.
The same experiments can be repeated with milk, provided that care is taken to bring it to a boil under pressure at a temperature of a hundred and a few degrees Celsius, using the apparatus shown in Fig. 10 and Fig. 10-bis, Pl. I, and to allow the flask to cool while heated air is introduced. The open flask can then be left to its own devices. The milk is preserved without alteration. I have been able to leave milk prepared in this way for several months in an oven at 25 to 30°C without it spoiling. Only a slight thickening of the cream is observed, due to direct chemical oxidation.
I know of nothing more conclusive than these experiments, which are so easy to repeat and can be varied in countless ways. I initially believed it was essential either to introduce heated air once during the cooling of the liquid in the flask, or to maintain the flask constantly at the same temperature so that ordinary outside air could only enter the flask by slow diffusion; but I later realized that all these precautions were excessive. During temperature changes, the movement of air is only felt with some intensity in the neck, and it is only there that the germs carried by the air can be deposited. Organized formations in the liquid can only be induced by a very abrupt agitation of the liquid.
Another method, which is most often successful in triggering the formation of these formations, consists of closing the tapered end of the flask immediately after, or better yet, during boiling. A vacuum is then created by the condensation of the water vapor. Then the closed end of the curved neck is uncorked, and outside air enters forcefully, carrying all its dust with it until it comes into contact with the liquid. In this case, a change in the liquid usually appears after a few days.
I must add that I currently have in my laboratory several highly perishable liquids, preserved for eighteen months in open vessels with curved and sloping necks, including several of those that were presented to the Academy of Sciences at its meeting of February 6, 1860, when I had the honor of communicating these new results to them.
The great advantage of this method is that it definitively proves that the origin of life in infusions brought to a boil is solely due to solid particles suspended in the air. Gases, various fluids, electricity, magnetism, ozone, known or unknown phenomena—there is absolutely nothing in ordinary atmospheric air, apart from its solid particles, that is the condition for the putrefaction or fermentation of the liquids we have studied.
Dr. Schwann, and those who repeated or modified his experiments, as I have already stated, had established that it is not oxygen, or at least oxygen alone, that is the condition for life in infusions, but something else, an unknown principle, which heat destroys (Schwann), which cotton filters (Schröder and Dusch), and which is destroyed by strong chemical reagents (Schultze). There the experiment stopped. These uncertainties and hesitations, traces of which we find in Mr. Schwann's Memoir, and especially in the work of Mr. Schröder, justified either the hypothesis of disseminated germs or the hypothesis of the existence in the air of a chemical or physical principle, a conclusion to which Mr. Schröder had settled.
In research of this nature, where the mind is unwittingly dominated by the impenetrable mystery of the origin of life on the Earth's surface, I do not believe that any hypothesis, however strange, can fail to gain credence. They can only be dismissed through well-studied and rigorously demonstrated facts. It is necessary, as the Commission for the prize proposed by the Academy states with both accuracy and authority, to "establish precise, rigorous experiments, equally studied in all their circumstances, and such, in short, that some result can be deduced from them, free from any confusion of the experiments themselves."
I have striven to give this character to my experiments. If I am not mistaken, those I have described in the preceding chapters truly prove what they claim to prove, which can be summarized in this twofold proposition:
1. There are constantly in the air organized particles that cannot be distinguished from the true germs of the organisms in infusions;
2. When these particles and their associated amorphous debris are sown in liquids that have been boiled and that would remain intact in previously heated air if this inoculation were not performed, the same organisms appear in these liquids that develop in open air (1).
Having established this, does a proponent of spontaneous generation wish to continue to uphold their principles, even in the face of this twofold proposition? He can still do so, but then his reasoning will inevitably be this, and I leave it to the reader to judge:
“There are solid particles in the air,” he will say, “such as calcium carbonate, silica, soot, strands of wool, cotton, starch, and alongside them, organized particles bearing a perfect resemblance to the spores of Mucedinaceae or to the eggs of Infusoria. Well, I prefer to place the origin of Mucedinaceae and Infusoria in the former, amorphous particles rather than in the latter.”
In my opinion, the inconsistency of such reasoning is self-evident. The entire progress of my research consists in having cornered the proponents of the doctrine of heterogenesis.
CHAPTER 7: It is not true that the smallest quantity of ordinary air is sufficient to give rise, in an infusion, to the organized productions [microorganisms] specific to that infusion. –Experiments on air from various locations. –Drawbacks of using a mercury bath in experiments related to so-called spontaneous generation.
I have already indicated in the historical section of this Memoir the influence that Gay-Lussac's famous work on the air in Appert's preserves, and on the interpretation that the illustrious physicist deduced from his experiments, had on the subject at hand. Here are his own words:
"One can be convinced, by analyzing the air in bottles in which substances have been well preserved, that it no longer contains oxygen, and that the absence of this gas is consequently a necessary condition for the preservation of animal and vegetable substances."
That the air in the preserves studied by Gay-Lussac was devoid of oxygen is beyond doubt. No one would dare question the accuracy of an air analysis performed by Gay-Lussac. However, it is beyond doubt today, although no one, to my knowledge, has followed up Gay-Lussac's experiments, that Appert's preserves can contain oxygen, especially when freshly prepared. The air analyses I reported on pages 36, 53, and 61 show that oxygen in the air, rendered inactive by heat according to Schwann's method, combines directly with organic matter, releasing carbonic acid, but this is a very slow process.
Nevertheless, direct oxidation does occur; this cannot be denied. This oxidation may be more pronounced in Appert's preserves during preparation due to the temperature increase. In any case, if the preparation leaves oxygen in the preserves, this gas will gradually disappear through the direct oxidation I have just described.
There is one circumstance that must greatly contribute to rendering the amount of oxygen remaining in Appert's preserves very low or nonexistent: it is the ratio of air to organic matter volumes. They always contain little air and a great deal of matter, a very favorable circumstance for the oxidation process to be completed. But, I repeat, nothing would be easier than to prepare preserves while leaving some oxygen in them, and there is reason to believe that they often do contain it. Schwann's experiment leaves no doubt in this regard.
This is why Gay-Lussac's interpretation of the results of his analyses, namely that the absence of oxygen is a condition for preservation, is entirely erroneous. Not everyone has been able to make this distinction between the truth of the facts observed by Gay-Lussac and the error of his interpretation. Dr. Schwann should rightly be considered the author of the true theory of Appert's processes. Appert's preserves continue to be preserved in the presence of heated air: this is his discovery. The secret of their preservation therefore lies in the destruction by heat of a principle contained in ordinary air, and not in the absence of oxygen (1).
< Footnote: (1) The mere fact of the absence of oxygen gas does not have to play a role in explaining the process; it should not be concluded from this that one could, in practice, safely leave a large amount of air in the preserves. For if the heat has not destroyed all the germs of infusoria and Mucedinaceae brought in by the air or matter, these still-fertile germs can develop if oxygen is present, whereas if this gas is absent, they will develop no more than if they had been truly deprived of life. But I think that what is always to be feared, and especially in cases where there is little oxygen, are the germs of plant or animal ferments, ferments that do not need air to live, and whose germs must necessarily be killed by heat. I am convinced that this is the danger that the preserver should most fear, and I am inclined to believe, for example, that the butyric infusorial animalcules that I recently described develop in certain poorly prepared preserves. End footnote >
But there is an extension of Gay-Lussac's experiments, which Schwann's discovery did not undermine, but rather served to confirm, an extension that the opponents of the doctrine of spontaneous generation have not contested, and on which the proponents of this doctrine rightly base one of their principal objections. Namely, that the smallest quantity of ordinary air, brought into contact with an infusion, quickly induces the formation of the Mucetidae and Infusoria typically found in that infusion.
This view has always been supported, at least indirectly, by the practice adopted and deemed essential by observers of meticulously keeping ordinary air out of their experiments. As we have seen, sometimes they recommend heating the ordinary air, sometimes they subject it to energetic chemical agents; often they first place all its parts in contact with water vapor at 100° (Spallanzani's experiment); finally, at other times they operate with artificial air [oxygen gas generated from water by means of electricity?], and, if it happens, under one of these various conditions, that the experiment gives rise to organized productions, they do not hesitate to assert that the operator has not been able to completely avoid the hidden influence of a small portion of ordinary air, however small it may be.
From then on, proponents of spontaneous generation hasten to point out, quite rightly, that if the smallest portion of ordinary air develops organisms in any infusion whatsoever, then it must necessarily follow, if these organisms are not spontaneous, that this tiny portion of common air contains the seeds of a multitude of diverse products; and that, finally, if this is the case, ordinary air, in the words of Mr. Pouchet, must be saturated with organic matter; it would form a thick fog.
This reasoning is certainly very sensible. It would be even more so if it were firmly established that the lower species that appear so distinct, are indeed distinct, and consequently originate from different germs. This is plausible, but it is not proven. There is, therefore, a serious difficulty here, seemingly very well-founded. But is it not the product of exaggerations and more or less erroneous facts? Is it true, as is generally accepted, that there is a continuity of the cause of so-called spontaneous generation in the Earth's atmosphere? Is it truly certain that the smallest quantity of ordinary air is sufficient to develop organized products in any infusion?
The following experiments answer all these questions. In a series of 250 cubic centimeter flasks, I introduce the same putrescible liquid (albuminous water from brewer's yeast; the same water sweetened; urine, etc.), so that it occupies approximately one-third of the total volume. I taper the necks with a flame, then I boil the liquid, and I seal the tapered end during boiling. A vacuum is thus created in the flasks [due to the cooling and condensing of the steam]; then I break off their tips at a specific point. Ordinary air rushes in violently, carrying with it all the dust particles it holds in suspension, and all the known or unknown substances associated with it. I then immediately seal the flasks with a flame and transfer them to an oven at 25 to 30°C, that is to say, to the best temperature conditions for the development of the animalcules and Mucors.
Here are the results of these experiments, which contradict generally accepted principles and, on the contrary, perfectly support the idea of germ dispersal. Most often, in just a few days, the liquid deteriorates, and the most varied organisms appear in the flasks, even though they are placed under identical conditions—far more varied indeed, especially with regard to Mucetaceae and Torulaceae, than if the liquids had been freely exposed to ordinary air.
But, on the other hand, it frequently happens, several times in each series of tests, that the liquid remains absolutely intact, regardless of the duration of its exposure in the oven, as if it had received heated air.
This method of experimentation seems to me as simple as it is irreproachable for demonstrating that ambient air does not, by any means, continuously provide the cause of so-called spontaneous generation, and that it is always possible to collect, at a given place and time, a considerable volume of ordinary air, having undergone no kind of physical or chemical alteration, and yet entirely unsuitable for giving rise to Infusoria or Mucedinea, in a liquid that deteriorates very quickly and constantly upon free contact with air.
The partial success of these experiments also tells us sufficiently that, due to the movement of the amosphere, a sufficient quantity of air will always pass over the surface of a liquid placed boiling in an open vessel for it to receive germs capable of developing there within two or three days.
I said that the production is more varied in flasks than if the contact with the air were unrestricted. Nothing could be more natural, for by limiting the air intake and repeating it many times, one captures, as it were, the germs in the air with all the variety in which they are found there. A small number of germs, in a limited volume of air, are not hindered in their development by more numerous germs or those with earlier fertility, capable of invading the space, leaving room only for themselves.
Thus, Penicillium glaucum, whose spores are durable and widespread, appears alone after very few days in unenclosed liquids, which, on the contrary, offer very diverse productions when subjected to limited quantities of air.
Finally, it is very interesting to note the differences observed in the number of negative results from these experiments, depending on atmospheric conditions. Here again, we find striking confirmation of the opinion I am defending. Indeed, nothing is easier than increasing or decreasing either the number of flasks that deteriorate or the number of flasks that remain intact. This will become clear from the details I am about to provide.
A. – Preliminary experiments designed to highlight the fact of the non-continuity of the cause of so-called spontaneous generations.
On May 26, 1860, I opened and immediately closed two flasks on an open-air terrace, a few meters above the ground. One flask contained yeast water, the other the same liquid sweetened to a ratio of 1/10 [I guess that means 1 gram of sugar per 10 milliliter of yeast water]. This occurred a few moments after a light and very brief rain shower. On June 1, there was no sign of organized growth. On the 2nd, a very small clump of mold appeared in one of the flasks, the one containing the sugar yeast water. On the 8th, the second flask also showed a small clump of mold. Both liquids were perfectly clear and remained so during the growth of the mycelia (1).
< Footnote: (1) I will point out here an instructive fact that seems to me to be in complete agreement with the general results of this work. Referring to the details of the experiments in Chapter IV and following, it will be seen that it has never happened that, by sowing cotton or asbestos wadding, laden with dust from a large volume of air, in various infusions, organized growth did not appear the very next day or the day after. In the experiments of this chapter, on the contrary, it is observed that growth sometimes takes a considerable amount of time to manifest itself—eight, twelve, fifteen days. This is quite understandable. In the first case, so many germs are sown that there are always some whose fertility is almost as early as that of the healthiest germs of this type of production. In the second case, where the seeds are ultimately sown in a very limited volume of air, it must often happen that those which enter the flask are in poor condition, and their development is made difficult by all the causes of alteration to which they must have been exposed in the atmosphere. End footnote >
On May 28, 1860, I opened and closed four flasks on the same terrace after a violent downpour with very large raindrops. On June 4, there was no sign of production. On the 5th, a small clump of mold appeared in one of the flasks. The liquid was very clear. On the 6th, another clump of mold appeared in a second flask. The liquid was very clear. The other two flasks remained intact and very clear. The same condition was observed in 1861.
On July 20, 1860, I opened and closed six flasks containing yeast water in one of the rooms of my laboratory. Even today (April 1861), the liquid in four of these flasks is perfectly clear, without the slightest sign of organized production. The other two promptly offered productions, on July 22nd and August 1st. In one, Infusoria and Torulacea; in the other, silky ball mycelium.
On June 30, I opened and resealed a large number of flasks containing unsweetened yeast water, with the aim of studying under a microscope the organisms that would develop, in order to get an idea of their variety. I have reproduced Fig. 27, Pl. II. A, B, C, D, E, F, G, H, K, L, M, several of my drawings.
A, Bacterium 0.0006 mm in diameter and 0.005 mm at its longest point (1).
B. Torulaceae in very small globules, perfectly spherical, 0.0015 mm in diameter, and arranged in small chains.
C. Mucor and Vibrios.
D. Torulaceae, whose cells have a diameter of 0.004 to 0.007 mm. It is quite common, as I have already had occasion to mention.
E. Mycoderma similar to that of beer, wine, etc., in segments of all sizes, and more or less branched.
F. Infusoria of infinite smallness. The smallest of the Monads moves with extraordinary agility. They are barely perceptible points.
G. Torulaceae in beautiful budded globules, slightly granular inside, whose diameter varies from 0.006 to 0.009 mm. It perfectly resembles brewer's yeast; It also closely resembles Torulaceae D, but it is slightly larger and slightly more granular.
H. Torulaceae in viscous granules, which adhere strongly to the walls of the flask, are difficult to detach, and form a continuous layer. The diameter of the granules is exactly that of Torulaceae B; but the latter is in the form of strings and does not adhere to the vessels. I believe they are distinct species, despite their resemblance.
K. Alga formed of quaternary cells, deposited as a precipitate on the walls of the flask; under the microscope, it resembles layers of stone. Under the influence of hydrochloric acid diluted with water, the clusters of cells separate into small groups of four cells.
L. Mucorea in a reddish film extending across the surface of the liquid, tearing very easily, and falling in shreds to the bottom of the liquid where it has the appearance of a rag. When crushed under a small glass slide, under the microscope it presents clusters of the finest granules, teeming in the channels that separate these clusters.
M. Mucor in very fine granules, mixed with Vibrios of varying lengths, with sinuous movements.
Add to these figures, in which I have preferably represented the Mucors, Torulaceae, and the most frequent Infusoria, drawings of a multitude of mycelia in septate tubes that then spread across the surface of the liquid in thick, moist, gelatinous membranes, or in membranes composed of a network of tubes and covered with spores of green, orange-red, yellowish-green, brownish-black, etc., colors, offering the most varied species, and you will have an idea of what distinct species yeast water, placed under the influence of limited quantities of ordinary air in a series of flasks prepared as I have indicated, can produce.
These are the same species that the same liquid would produce in free contact with air; but to recover them all, it would be necessary to multiply the trials further, because limited air intakes are much more likely, as I have already said, to capture the germs from the air with all the variety to which they are accustomed.
Therefore, I am always very surprised when Mr. Pouchet, in his skillful arguments in favor of the doctrine of heterogenesis, returns to this vague objection concerning the generative capacities of infusions stifled by the material conditions of in vitro experiments. These generative capacities, to use Mr. Pouchet's expression, I see as enhanced rather than destroyed. If this objection had any merit, it should be directed at Schwann's experiments, whose results are essentially negative, and not at all at mine. because one of the advances of my research is to have instituted experiments which have, at the will of the operator (as seen in chapter IV) positive or negative results.
But in this respect of the variety of productions, I acknowledge that there is a very great difference between those of a plant nature and others. The former are very numerous, while for Infusoria this is limited to Monads, Bacterium, and Vibrio. Without wishing to prejudge here the question of the origin of large Infusoria, on which I hope to publish a separate work, it is well known that an infusion never yields large Infusoria at first, that Paramecia, Kolpoda, Vorticella, etc., never precede Bacterium and Vibrio.
Therefore, if one refers to the air analyses that I present in this Memoir, when the smallest Infusoria appeared in the flasks, one will see with what rapidity they alter the air and charge it with carbonic acid.
As long as there is moisture, life is endless in an infusion exposed to open air, because oxygen, one of the essential nutrients for Mucetidae and Infusoria, is never lacking. But in a confined atmosphere, life inevitably ceases after a few days. Larger Infusoria will therefore not appear, since it is recognized that life does not begin in infusions with them. Their appearance would present a new difficulty to resolve.
But this in no way invalidates the conclusions I have reached regarding the origin of Mucorea, Mucetidae, Toruiaceae, and the smallest Infusoria in infusions that have been brought to a boil beforehand. On this point, the only one I am addressing today, I consider the results of my work to be irrefutable.
B. – Experiments on still air.
Thanks to the kindness of Mr. Le Verrier, I was able to conduct some experiments on the air in the Observatory's cellars. In this part of the cellars, located in the zone of constant temperature, the perfectly still air must obviously allow its dust to settle to the surface of the floor during the intervals between disturbances that an observer might cause through their movements or the objects they are carrying. Therefore, by multiplying precautions when going down to take air samples, the number of flasks that subsequently show no organized production should be considerably greater than if they had been filled, for example, with air in the courtyard.
This is indeed what happens, and the meaning of the results, in accordance with the nature or the greater or lesser number of precautions taken to avoid the accidental introduction of foreign dust, compels us to admit that if the flasks were opened and closed in the cellars without the operator having to go there, the air in these cellars would constantly appear as inactive as air heated to a red-hot temperature.
However, this is not to say that it possesses, in itself, and given the conditions in which it is placed, any inherent inactivity. On the contrary, being saturated with humidity, and since most lower organisms have no need of light to live, this air has always seemed to me more suitable than that of the ground surface for the development of these organisms.
I will only report one series of experiments. On August 14, 1860, I opened and resealed ten flasks containing yeast water in the cellars of the Observatory, and eleven other flasks of the same preparation in the courtyard of the establishment, 50 centimeters above the ground, in a light breeze. All were brought back the same day to the incubator in my laboratory, which has a temperature of 30°C. I have kept all these flasks to this day. Only one of those opened in the cellars contains a plant culture. The eleven flasks opened in the courtyard all yielded Infusoria or plants of the kind I have already described.
C. – Experiments on air at various heights.
The experiments described in the preceding paragraphs sufficiently establish that there is no continuity in the atmosphere as the cause of so-called spontaneous generation; that is to say, it is always possible to take, from a specific location, a significant but limited volume of ordinary air, having undergone no kind of physical or chemical modification, and entirely unsuitable for causing any alteration whatsoever in a highly putrescible liquid.
From this stems the principle that the primary condition for the appearance of living beings in infusions or fermentable liquids does not exist in air considered as a fluid, but that it is found here and there, in places, offering numerous and varied breaks in continuity, as one would expect in the hypothesis of the dissemination of germs.
It seemed very interesting to me to follow the ideas suggested by the preceding results, by subjecting air taken at various altitudes to the experimental method I described. I could have ascended in a balloon; but for preliminary, trial studies, I thought it would be more convenient and perhaps more useful to conduct comparative tests in the plains and in the mountains.
I had the honor of presenting to the Academy, at its meeting of November 5, 1860, seventy-three flasks, each with a capacity of 1/4 of a liter, prepared as I described at the beginning of this chapter, that is to say, they were initially emptied of air and filled one-third full with yeast water, filtered to perfect clarity.
Twenty of these flasks received air in the countryside, quite far from any habitation, at the foot of the hills that form the first plateau of the Jura Mountains; another twenty received air on one of the Jura mountains, at 850 meters above sea level; finally, another set of twenty of these same flasks was transported to Montanvert, near the glacier, at an altitude of 2000 meters.
Here are the results they yielded: Of the twenty flasks opened in the countryside, eight contained organized products; of the twenty flasks opened on the Jura Mountains, only five contained them; and finally, of the twenty flasks opened at Montanvert, by a fairly strong wind blowing from the deepest gorges of the Glacier des Bois, only one was spoiled.
These experiments should undoubtedly be multiplied considerably. But as they stand, they already tend to prove that as one ascends, the number of germs suspended in the air decreases noticeably. Above all, they demonstrate the purity, from our perspective, of the air on the high, ice-covered peaks, since only one of the vessels opened at Montanvert gave rise to a Mucédinea.
Intake requires certain precautions that I had long recognized as essential to minimize the impact of dust carried by the operator and dust present on the surface of the flasks or tools to be used. First, I heat the neck of the flask and its tapered tip quite strongly in the flame of an alcohol lamp, then I scratch a line on the glass with a steel blade. Next, raising the flask above my head, in a direction opposite to the wind, I break the tip with iron tongs, the long prongs of which have just been passed through the flame, in order to burn off any dust that might be on their surface and which would inevitably be partially blown into the flask by the sudden influx of air.
During my journey, I was quite concerned that the agitation of the liquid in the flasks during transport might have some detrimental effect on the initial development of the Infusoria or Mucor. The following results dispel these concerns. They will also allow us to recognize the significant difference between the air of the plains or highlands and that of inhabited areas.
My first experiments on the Glacier des Bois were interrupted by a circumstance I had not foreseen. I had brought along an aeolipile lamp fueled by alcohol to seal the tips of the flasks after they had been opened; however, the whiteness of the ice struck by the sun was so great that it was impossible for me to distinguish the jet of burning alcohol vapor, and as this jet of flame was also somewhat agitated by the wind, it never remained on the broken glass long enough to melt the tip and seal the flask hermetically. All the means that I could have had at my disposal at that time to make the flame visible, and consequently steerable, would inevitably have given rise to causes of error, by spreading foreign dust in the air.
I was therefore obliged to return to the small inn at Montanvert, still unsealed, the flasks I had opened on the glacier, and spend the night there, in order to operate under better conditions the following morning with other flasks. It is the results of this second series of experiments that I indicated earlier.
As for the thirteen flasks opened the previous day on the glacier, I only resealed them the following morning, after they had been exposed all night to the dust of the room in which I had slept. Now, of these thirteen flasks, ten contain Infusoria or molds. Since the number of flasks affected in these first tests is greater than in those that followed, the agitation of the liquid during the journey did not have the influence on the development of the germs that I had feared.
Furthermore, the proportion of flasks that, in these initial experiments, yielded organized growth, provides irrefutable proof that inhabited places contain a relatively considerable number of fertile germs, due to the dust that settles on the surface of all objects. In this small inn at Montanvert, for example, there is certainly dust and consequently germs from all over the world, brought in by travelers' belongings.
D. – Experiments on mercury.
I have already recalled in Chapter VII and in the historical section of this Memoir how Dr. Schwann's experiment had ruled out Gay-Lussac's hypothesis on the role of air in explaining Appert's preservation processes.
But how is it that in the famous chemist's experiment on grape must, an experiment so often cited, brewer's yeast arises following the introduction of a very small portion of air, and that, if this same experiment is repeated on various infusions, these are seen to spoil under the influence of minimal quantities of air, much more so by the introduction of heated or artificial air; for Mr. Pouchet's experiments, carried out with the mercury bath, are accurate, while Schwann's are almost constantly erroneous?
It is simply that the mercury in our baths, which only occasionally undergoes washing by strong acid, is usually filled with germs brought in by dust suspended in the air. This dust falls into the bath every time it is exposed to air and penetrates the mercury through handling, without its specific lightness being able to bring it all back to the surface due to its microscopic volume (1).
Footnote: (1) It is clear that in Gay-Lussac's particular experiment, where the test tubes he used were not preheated, the germs could have been introduced by dust on the surface of the glass of the test tubes, or by the grapes, which, like all objects, are covered with dust and consequently with germs.
Here is a very simple and demonstrative experiment that is almost always successful. Take one of these flasks, prepared as I described at the beginning of Chapter VII, emptied of air and partially filled with a putrescible liquid that has been previously boiled. Place its closed tip into the bottom of any mercury bath, and break its tip at the bottom of the bath. Organized growth will occur in the liquid of this flask, perhaps nine times out of ten, after introducing either heated air or artificial air.
Obviously, only mercury could have provided the germs, unless there is spontaneous generation. However, this hypothesis is ruled out by the fact that if the experiment is repeated without the use of the mercury bath, as in Chapter III, following the method shown in Fig. 10, Pl. I, there are no productions.
The following experiments are even more direct and conclusive. I take mercury, drawn without any particular precautions, from the bath of any laboratory, and, using the method I described earlier in Chapter IV, within an atmosphere of heated air, I deposit a single globule of this mercury, the size of a pea, into a perishable liquid. Two days later, in all the experiments I conducted (1), there were varied results; and when repeating the same tests at the same time, using the same method, without changing anything in the procedure, on mercury from the same source, but which had been heated, there was not the slightest result.
Footnote: (1) Four in total: two with mercury from my laboratory, one with mercury from the chemistry laboratory of the École Normale, and another with mercury from the physics laboratory of the same institution.
We must not exaggerate the consequences that can be deduced from these experiments. Let us examine what happens. Mercury is drawn from a bath into a stemmed glass; in this way, unless precautions were taken (which I do not assume were taken), a portion of the mercury that is on the surface of the bath, where there is dust, is always collected; then a drop of this mercury is poured into a small tube. The experiment shows that this drop, as it falls, carries a significant portion of the dust from the surface of the mercury in the glass onto its surface. The collected drop therefore always contains some of the dust from the surface of the bath.
I will be even clearer if I note that if a drop of mercury, covered on its surface with a layer of any kind of dust, were to flow from a stemmed glass, the entire drop, as it fell, would be enveloped by a layer of this dust, due to capillary action. But nothing would be simpler than to repeat the experiment on a globule of mercury taken with special precautions from within the mass of the liquid. I have no doubt that the experiment would still succeed in the most ordinary way, even under these particular conditions.
CHAPTER 8: Comparative action of temperature on the fertility of spores of Mucedinea and germs that exist in suspension in the atmosphere.
The experiments I am about to describe add further confirmation to the definitive conclusions of this Memoir. What is known about the resistance to death of seed-gall nematodes, rotifers, and also the seeds of higher plants after prior desiccation [drying], tells us sufficiently that the spores of the Mucedinaceae family should be able to retain their fertility at fairly high temperatures when they are dry.
Let us suppose for a moment that we determine the temperature limits that the spores of common Mucedinaceae can withstand without being destroyed, and the limits beyond which all vitality ceases in these small seeds. If the organized corpuscles that constantly exist in suspension in the air, and among which there are always a great many that have a perfect resemblance to Mucedinaceae spores, if, I say, these corpuscles are indeed really spores, then experience should lead us to this curious result: that dust from the air sown in Appert preserves, according to the method represented in Fig. 12, Plate I, will still be fertile after they have undergone the highest temperature that common Mucedinaceae spores can withstand, and that they will have no effect on these same preserves if they have been previously subjected to the temperature that kills these spores.
Let us first examine what is known on this subject. Duhamel reports in one of his works that he was able to germinate wheat that had withstood a temperature of 100°C. This observation by the learned agronomist became the basis for some of Spallanzani's research on the degree of heat to which seeds can be subjected without losing their ability to germinate. Among higher plants, he studied five species of seeds: chickpea, lentil, spelt, flaxseed, and clover. Spallanzani also investigated the influence of temperature on the spores of the Mucedinaceae family.
As for the seeds of higher plants, Spallanzani's results, while quite curious, should not surprise us given the current state of our knowledge. The clover seed, less sensitive than all others, could withstand a temperature close to 100°C. But for the seeds of molds, Spallanzani was led to singular conclusions. He admits, in fact, that not only can the spores of the Mucedinaceae family withstand a temperature of 100°C when immersed in water, but that they can even resist the heat of a blazing fire when dry. Moreover, in this latter case, he does not specify the temperature precisely (1).
< Footnote: (1) The following passage from Spallanzani's works is taken from a chapter in Volume II of his Opuscules, in which his main aim is to prove that Michelli was right to consider the dust that falls from molds when they are ripe as being the seed of these plants. “The tiny grains that emerge from the heads of mature molds, and which are the true seeds of these plants, have the unique property of withstanding a degree of heat that no other seed can withstand without losing its ability to germinate. After boiling these tiny grains in water, I poured the water, which had turned black, onto objects capable of molding, and, following the usual results of these kinds of experiments, the mold grew thicker than on the same objects that had not been moistened. I did the same thing with dust exposed to a much stronger fire, such as that of a blazing fire, and I found that this heat does not deprive these seeds of their ability to reproduce.” End footnote >
It would be difficult to understand why Spallanzani's results on the seeds of the Mucedinaceae were not subjected to further testing if the experiments did not present particular difficulties, mainly in finding a rigorous experimental method. Nothing could be simpler for higher plants than to test whether their seeds are still capable of germinating when heated to a specific temperature: wheat only grows where it has been sown; but Mucedinaceae develop wherever they encounter favorable conditions. It is therefore essential, with regard to common Mucedinaceae, to use a method that allows us to definitively state that the small plant was reproduced by the spores that were sown, and not additionally by spores suspended in the air or deposited on the surface of the objects used in the experiment.
Here is the method I followed, which seems to me irreproachable: I pass a little asbestos into the small heads of the mold I wish to study; then I place this spore-covered asbestos in a very small glass tube, which I insert into a larger diameter U-shaped tube, where the small tube can move freely, Fig. 28, Plate I.
One end of the U-shaped tube is connected by a rubber stopcock to a T-shaped metal tube with valves. One of the valves connects to the pneumatic machine, another to a red-hot platinum tube. The other end has a rubber stopcock that also receives the flask in which the spores are to be sown, a flask sealed with a flame, filled with heated air and a liquid previously brought to a boil, which will serve as food for the young plant.
Finally, the U-tube is immersed in a bath of oil, ordinary water, or water saturated with various salts, depending on the desired temperature for the spores. Between the U-tube and the platinum tube, there is a desiccant tube containing sulfuric acid. [The sulfuric acid absorbs water from the air and keeps humidity in the tubes close to 0%, so that the spores are kept completely dry. Thus, when the U-tube containing the spores are submerged in a bath of boiling water or salt water or oil, the air inside the U-tube is heated to the boiling temperature, and the spores in the U-tube are subjected to dry heat. I don’t know how exactly the desiccant tube works, if the air is supposed to somehow move through the sulphuric acid or if it works in another way.]
Once the entire apparatus preceding the platinum tube has been filled with heated air and the spores have been maintained at the required temperature for a sufficient, adjustable time, the tip of the flask is broken with a hammer blow, without untying the rubber cords connecting the flask to the U-tube. Then, with the U-tube tilted appropriately away from its bath, the asbestos and its spores are slid into the flask. Finally, the flask is sealed by a flame through one of the constrictions on its neck. It is then placed in an oven at a temperature of 20° to 30°, which is very favorable to the rapid development of Mucedinaceae.
Footnote: (1) When, in a flask prepared as I described in Chapter VII, p. 74, only one mold develops, which is frequent, it is evident that the spores are perfectly pure. It was in the sporangia of such molds that I passed the small asbestos brush, after having removed the upper part of the flask. There was no chance of introducing foreign germs except during the very brief time I was collecting mold spores to transfer them into the U-tube. The asbestos was heated intensely before being coated with spores, as was the U-tube. As soon as it had cooled, the small tube and its spores were placed inside. The experiment on airborne dust is carried out in the same way with asbestos that has been exposed to an ordinary air current, following the instructions in Chapter II.
I will now go into detail about the results of a few specific experiments. On June 1, 1860, I placed a piece of cotton, laden with ordinary air dust, into a flask containing yeast water and heated air since March 19, without having noticed the slightest alteration. This cotton [with dust] had been kept for one hour at 100°C (in a boiling water bath).
During the night of June 4-5, a kind of powdery deposit began to appear on the walls of the flask and rapidly covered the surface of the liquid in the following days. It was a colorless Mucorea, in a slightly mottled film, in small, vaguely circular clumps as if lifted by gas bubbles, which was merely an illusion. By June 9 or 10, all development had ceased, and the film had fallen to the bottom of the flask in shreds.
At the end of June, I opened the flask to study this Mucorea under the microscope. It is composed of granules, as is generally the case with all Mucorea species, but here the granules are relatively large. Their diameter is 0.002 mm. These granules were isolated or in clusters, shiny at their centers, with clearly defined outlines. Fig. 29, Plate II, shows them associated with a few very fine Vibrio bacteria, barely visible, which were no longer moving when the flask was opened. They were very few in number. This experiment shows that the dried germs of these two productions can withstand a temperature of 100°C for one hour.
On June 2, 1860, I placed a small wad of asbestos, laden with airborne dust, in milk that had been stored since April 10 in the presence of heated air, without any alteration. The wad had been exposed to 100°C (boiling water bath) for fifteen minutes. On June 4, the milk had not curdled, but a nearly translucent layer of whey was visible on its surface, indicating spoilage. On June 5 and 6, it was evident that the milk was spoiling. A yellowish, caseous deposit was present at the bottom of the flask, with no apparent release of gas. I had not yet encountered signs of milk spoilage exactly like these.
On June 7th, I opened the flask and examined the liquid under the microscope. It was found to be filled with a multitude of infusoria of two very distinct types. Some were very agile, thread-like Vibrio species that ran rapidly, causing the second half of their body to tremble sharply. They were 0.006 to 0.009 mm long and 0.0007 mm wide. Others were short, much wider, somewhat constricted, and often joined in chains of two or three segments. The segments were 0.003 to 0.004 mm long and 0.002 to 0.003 mm in diameter. Fig. 30, Plate II, shows these two types of infusoria in addition to the butter [milk fat] globules. No gas was released when I opened the flask in the mercury bath.
On July 6th, I placed a wad of asbestos with dust, heated for half an hour at 100°C (boiling water bath), into a flask containing sugar yeast water mixed with chalk, which had been preserved unaltered since April 11th in the presence of heated air. On July 8th, the solution became noticeably cloudy, with a thin film on all the walls. On July 10th, it became milky cloudy, with crumpled fragments in the liquid and at the bottom. There appeared to be gas being released.
On July 10th, I opened this flask; a sudden and violent release of gas occurred. It is evident that fermentation has taken place. Under the microscope, two species of Vibrio were observed, differing mainly in the diameter of their segments. Some have a diameter of 0.0006 to 0.0008 mm; others have a diameter of 0.0015 to 0.002 mm and a length of up to 0.01 mm and more (1).
Footnote: (1) I have no doubt that the fermentation of the liquid in this flask was caused by these latter infusoria, preserved from contact with air by those of the first species, which were ordinary Vibrio bacteria, needing air to live. See my communication of February 25, 1861, to the Academy of Sciences on the discovery of the infusorial animalcule that produces butyric fermentation.
On November 9, 1860, I placed a wad of asbestos, laden with airborne dust, into a flask containing yeast water, and another similar wad into a second flask containing urine. These flasks had been stored since June 25. Before introducing the wads into the flasks, they had been kept for half an hour at 121°C (oil bath).
On November 11, the flask of yeast water began to show a clump of mycelium in very loose tubes, which grew with extraordinary rapidity. Within four days, it reached the level of the liquid and grew everywhere, producing long, cotton-like tubes of great whiteness that quickly spread up the walls of the flask. The spores and the tubes bearing them are shown in Fig. 31, Plate II.
The urine flask only began to show a small clump of mold in tightly packed tubes on November 16th, in the form of a small, silky ball. This Mucedinea developed so slowly that by November 22nd it was still less than the size of a pea. On the same day, November 22nd, another mycelium appeared in loose tubes, which smothered the first one in a few days. No infusoria were found in either case.
On August 12, 1860, the same experiment was performed, using yeast water and dust from the air that had been previously heated for half an hour in an oil bath at 129°C. Today (April 1861), there is still no sign of organized growth.
Let us now review some experiments on the spores of the common Mucedinaceae. On July 21, 1860, I placed a small wad of asbestos, loaded with Penicillium spores, into a flask containing yeast water and heated air, without any alteration, since June 26. The spores had been previously heated for half an hour in an oil bath at 119 to 121°C.
On July 22, 23, and 24, there was no sign of development. On July 25, a multitude of very small tufts of mycelium covered the walls of the flask. But, rather strangely, only the spores at the bottom had developed. Those that, at the time the asbestos wadding was introduced, had risen to the surface to form clumps, a kind of blotch, did not germinate at all; they did not develop germ tubes.
On July 26, there was noticeable, though somewhat weak, development of the clumps at the bottom. The spores on the surface of the liquid had not yet germinated. On July 28, several patches had developed on the surface, but they originated from clumps at the bottom and not from surface spores. These patches began to fruit and turn green in their centers. Here and there on the surface, patches of ungerminated spores could still be seen. On August 3, the entire surface was covered by a beautiful, vigorous, bluish-green Penicillium. There was no indication that it was diseased. However, it must be noted:
1. That the spores, sown on July 21st, only began to germinate during the night of July 24th to 25th, whereas, if they had not been heated, or even if they had been heated to 100°C, they would have begun to show tufts of germ tubes visible to the naked eye the very next day; I have often observed this through direct testing.
2. Many spores had evidently been deprived of life, and being lighter, one might say, than the others, they had risen to the surface where they did not germinate.
Here is an experiment that will prove that by raising the temperature of the spores to 108.4°C instead of 120°C, germination occurs after just forty-eight hours. On July 23rd, I placed, in one of the yeast water flasks preserved since June 26th without alteration, a wad of asbestos loaded with Penicillium spores, which had been preheated, dry, as in all these experiments, for half an hour at 108.4°C (a bath of boiling, saturated salt water). The inoculation took place at noon on July 23rd.
By the 25th, at five o'clock in the evening, countless clumps of mycelium could be seen at the bottom of the liquid. It is therefore beyond doubt that, under the influence of high temperature, in the absence of any humidity, the fertility of Penicillium glaucum spores is preserved up to 120°C and even slightly higher, and that they reproduce a plant identical to the parent plant, and whose spores are fertile (I have observed this through direct testing). However, it is no less true that the viability of the germ is somewhat affected, and that the spores experience a noticeable delay in their germination capacity.
On August 12, 1860, I repeated the previous experiments on two flasks of yeast water that had been stored for a long time, using spores of Penicillium glaucum and spores of Ascophora elegans, heated for half an hour at 127°C to 132°C (oil bath). There was no spore development whatsoever in either flask.
In summary, I believe I can conclude from my experiments that the spores of common Mucedinaceae, heated in a vacuum or in dry air, remain fertile after being brought to a temperature of 120°C. It would probably be found that one could even go a little higher, perhaps to 125°C. Conversely, a fairly short exposure to 130°C is sufficient to render the spores of these same Mucedinaceae, which appear to be the most vigorous and the least sensitive, unfertile.
On the other hand, we find that the limits are the same for the fertility of airborne dust; that is, it produces Mucedinaceae even after being heated to 120°C, and it ceases to do so if subjected to a temperature of 130°C. The correlation of these results is further proof of the existence of Mucedinaceae spores among the organized particles that the microscope allows us to so easily identify in dust suspended in ordinary air.
CHAPTER 9: On the mode of nutrition of the ferments properly so-called, of the Mucedins and Vibrios.
It is essential to note that, until now, all experiments in spontaneous generation have involved infusions of plant or animal matter—in short, liquids containing substances that previously belonged to an organism. Regardless of the preliminary temperature and boiling conditions to which these substances are subjected, they possess a constitution and properties acquired under the influence of life. This fact has served as the basis for all theories on spontaneous generation.
However, I will demonstrate in this chapter that the appearance of lower organisms does not necessarily presuppose the presence of plastic organic matter, of those albuminoid substances that chemists have never been able to produce, and whose formation requires the participation of vital forces. The new experiments I am about to present will demonstrate the lack of foundation for all theories on the spontaneous formation of lower organisms.
Let us first examine these theories in which imagination plays such a large part, and in which the true principles of the experimental method play so little. Needham believed in the existence in organic matter of a particular force which he called vegetative force, and which survived the death of plants and animals. Specifically determined in an individual, it preserved its form and properties during its life. But at its death, it became free, and its manifestations depended on the particular conditions in which the disjointed parts of the individual's body were placed. And it was thus that this force, persisting in the organic matter of infusions, reorganized this matter according to modes that depended only on the conditions proper to the infusion (1).
Footnote: (1) See Spallanzani, Opuscules. Exposition of the new ideas of Mr. de Needham on the system of generation, Book 1, Chapter 1.
Buffon's system of organic molecules has much in common with Needham's ideas. I will reproduce verbatim the great naturalist's views on spontaneous generation (2).
Footnote: (2) Supplément. (Histoire de l’Homme. 1778, t. VIII, édition in-12.)
"My research and experiments," said Buffon, "on organic molecules demonstrate that there are no pre-existing germs, and at the same time they prove that the generation of animals and plants is not univocal; that there are perhaps as many beings, whether living or plant, that reproduce through the fortuitous assembly of organic molecules as there are animals or plants that can reproduce through a constant succession of generations..."
"Organic molecules, always active, always subsisting, belong equally to plants and animals; they penetrate raw matter, work it, stir it in all its dimensions, and make it serve as the basis for the fabric of the organization, of which these living molecules are the sole principles and instruments; they are subject only to a single power which, although passive, directs their movement and fixes their position. This power is the inner mold of the organized body; the living molecules that the animal or plant draws from food or sap assimilate to all parts of the inner mold of their body, they penetrate it in all its dimensions, they bring vegetation and life to it, they make this mold living and growing in all its parts; the inner form of the mold only determines their movement and their position for nutrition and development in all organized beings."
"And when death extinguishes the fire of organization, that is, the power of this mold, the decomposition of the body follows, and the organic molecules, all of which survive, finding themselves free in the dissolution and putrefaction of bodies, pass into other bodies as soon as they are drawn by the power of some other mold, so that they can pass from animal to vegetable and from vegetable to animal, without alteration and with the permanent and constant property of providing them with nutrition and life; only an infinite number of spontaneous generations occur during this interlude, where the power of the mold is without action, that is, during this interval of time during which the organic molecules are free in the matter of dead and decomposed bodies, as long as they are not absorbed by the internal mold of the organized beings that compose the ordinary species of living or vegetative nature; these organic molecules, always active, work to stir the putrefied matter, they appropriate some raw particles and, by their combination, form a multitude of small, organized bodies, some of which, like earthworms, fungi, etc., appear to be fairly large animals or plants, but others, almost infinite in number, can only be seen under a microscope. All these bodies exist only through spontaneous generation, and they fill the gap that nature has placed between the simple living organic molecule and the animal or plant; thus, one finds all the degrees, all the imaginable nuances in this sequence, in this chain of beings that descends from the most highly organized animal to the simply organic molecule; taken alone, this molecule is very far removed from the nature of the animal. Taken several together, these living molecules would be just as far removed from it, if they did not appropriate raw particles and arrange them in a certain form, approaching that of the internal mold of animals or plants. And since this arrangement of form must vary infinitely, both in number and in the different actions of living molecules against inanimate matter, it must result, and indeed does result, in beings of all degrees of animality. And this spontaneous generation, to which all these beings equally owe their existence, is exercised and manifested every time organized beings decompose; it is exercised constantly and universally after death and sometimes also during their lives, when there are some defects in the organization of the body that prevent the internal mold from absorbing and assimilating all the organic molecules contained in the food. These superabundant organic molecules, which cannot penetrate the animal's internal mold for its nutrition, seek to unite with some particles of the inanimate matter of the food and form, as in putrefaction, organized bodies; this is the origin of tapeworms, roundworms, and flukes.”
A botanist, Mr. Turpin, has recently reproduced a system that bore a strong resemblance to Buffon's system of organic molecules. (See his Memoir in Volume XVII of the Memoirs of the Academy of Sciences.)
I now come to Mr. Pouchet's system (1).
Footnote: (1) Treatise on Spontaneous Generation. 1859, p. 335 et seq.
"One can consider," he said, "as a fundamental law that phenomena of fermentation or catalytic degeneration precede or accompany all spontaneous generation." "Organisms only arise from the very act of expiring nature, and at the moment when the elements of the beings from which they are generated enter into new chemical combinations and undergo all the phenomena of fermentation or putrefaction."
"It follows from this that primary generations only appear after the bodies from which they derive begin to undergo the first phenomena of decomposition, as if, in order to organize themselves, the new beings awaited the disintegration of the others, so as to seize the molecules of the expiring substance as they were released. It is evident that the organism draws its material elements only from the corpses of previous generations..."
"Thus, under the influence of fermentation or putrefaction, organized bodies decompose and dissociate their organic molecules; then, after having wandered freely for an unlimited time, when the plastic circumstances arise, these molecules regroup to constitute a new being...."
"Soon after the manifestation of the phenomena of fermentation and putrefaction, one observes that a film forms on the surface of the liquids under experiment, initially imperceptible and barely visible under the microscope; then this film thickens successively, and sometimes even becomes quite tenacious. This film is evidently composed of the remains of animalcules, first of the smallest order, and then of increasingly higher species in the Microzoa series. It is this same pseudo-membrane that I have called the proliferative film, because it is evident that it is this layer which, like an improvised ovary, produces the animalcules. Their development can be followed using our instruments, and it can be recognized that they are generated from the very organic debris of which they are composed.”
"The Protozoa, which initially form the proliferative pellicle, are Monads, Bacteria, and Vibrios. How are these animalcules produced? We cannot say, their extreme smallness making them inaccessible to any kind of investigation...."
"When plants appear on the surface of macerations, the pseudo-proliferative membrane is then formed almost entirely by the intertwining of mycelia, rudimentary fungi, which are observed on its surface. One could therefore add that there is a cryptogamic proliferative pellicle."
Through the union of parts of the proliferative pellicles, the ovules of lower organisms spontaneously form. Mr. Pouchet describes all the phases of the phenomenon. This is the system of the learned naturalist from Rouen, the work of a fertile imagination guided by erroneous observations.
By reporting here the principles of the systems on spontaneous generation that have had the greatest impact, my main aim is to show that, in all of them, the organic matter of the infusions plays an essential role. In itself, it would possess special properties acquired during its initial formation under the influence of life. Albuminoid substances would somehow retain a vestige of vitality, allowing them to organize themselves upon contact with oxygen when temperature and humidity conditions are favorable.
We will acknowledge that these opinions are entirely erroneous, and that albuminoid substances are merely a food source for the germs of Infusoria and Mucedinea; that they have no other role in infusions, as they can be replaced by crystallizable substances, such as ammonium salts and phosphates.
Thus, all theories concerning the spontaneous formation of the lowest organisms are deprived of one of their essential foundations. Experience has shown me, in fact, that in the experiments of Chapters IV, V, and VI, sweetened yeast water, urine, milk, etc., can be replaced by an infusion composed as follows:
Pure water: 100
Candy sugar: 10
Ammonium tartrate: 0.2 to 0.5
Ash of brewer's yeast: 0.1
If, in the presence of heated air, one sprinkles into this liquid the dust particles that exist suspended in the air, one observes the emergence of Bacterium, Vibrio, Mucetidae, etc. Albuminous nitrogenous matter, fats, essential oils, and the coloring substances specific to these organisms are formed entirely from ammonia, phosphates, and sugar.
Let us prepare the liquor in the same way with the addition of chalk:
Pure water: 100
Candy sugar: 10
Ammonium tartrate: 0.2 to 0.5
Ash of brewer's yeast: 0.1
Pure calcium carbonate: 3 to 5
The same phenomena will occur, but with a more pronounced tendency toward lactic, viscous, and butyric fermentations, and all the plant or animal ferments specific to these fermentations will arise simultaneously or successively. I will soon publish a detailed work on the results I obtained in these studies, which have always seemed to me to be of great interest for the question of so-called spontaneous generations.
It was through them that I was led to undertake the following experiments, the success of which exceeded my expectations. In pure distilled water, I dissolved a crystallized ammonia salt, candy sugar, and phosphates obtained from the burning of brewer's yeast; then I sowed into the liquid a few spores of Penicillium or some other Mucedinaceae.
These spores germinated easily, and soon, in only two or three days, the liquid was filled with flakes of mycelium, a large number of which quickly spread across the surface of the liquid where they fruited. The growth was anything but slow. By using an acidic salt of ammonia, the development of infusoria is prevented. Their presence would soon halt the growth of the small plant by absorbing oxygen from the air, which the Mucedinaceae cannot do without.
All the plant's carbon is derived from sugar, which gradually disappears completely; its nitrogen from ammonia; and its mineral matter from phosphates. Thus, on this point of nitrogen and phosphate assimilation, there is a complete analogy between ferments, Mucedinaceae, and the plants of a complex organism. The following facts will definitively prove this.
If, in the experiment I have just described, I remove any of the dissolved substances, growth ceases. For example, mineral matter would seem the least essential for organisms of this nature. However, if the liquid is deprived of phosphates, no growth is possible, regardless of the proportion of sugar and ammonium salts. Spore germination barely begins under the influence of the phosphates introduced in infinitesimally small quantities by the sown spores themselves.
Similarly, if ammonium salt is removed, the plant experiences no development. There is only a very feeble beginning of germination due to the presence of the albuminoid matter of the sown spores, even though there is an overabundance of free nitrogen in the surrounding air or dissolved in the liquid.
Finally, the same is true even if sugar, the carbon-rich food, is removed, even if there are any proportions of carbonic acid in the air or liquid. Everything indicates, in fact, that, with regard to the origin of carbon, the Mucedinaceae differ essentially from phanerogamous plants. They do not decompose carbonic acid; they do not release oxygen. On the contrary, the absorption of oxygen and the release of carbonic acid are necessary and continuous processes in their life. These facts give us precise ideas about the mode of nutrition of the Mucedinaceae, regarding which science does not yet possess any sustained observations.
On the other hand, and this is perhaps the most important point to note, they reveal to us a method by which plant physiology can easily address the most delicate questions concerning the life of these small plants, thus surely paving the way for the study of the same problems in higher plants.
Even if one were to fear that the results obtained from these seemingly insignificant organisms could not be applied to larger plants, there would nonetheless be great value in resolving the difficulties raised by the study of plant life, beginning with those where the slightest organizational complexity makes the conclusions easier and more reliable: the plant is reduced here, as it were, to the cellular level. The progress of science increasingly shows that the study of the processes carried out under the influence of plant or animal life, in their most complex manifestations, ultimately boils down to the discovery of the phenomena specific to the cell.