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Practical Criticisms

Practical Criticisms

Chapter:
(p.112) Chapter Seven Practical Criticisms
Source:
About Method
Author(s):
Jutta Schickore
Publisher:
University of Chicago Press
DOI:10.7208/chicago/9780226450049.003.0008

Abstract and Keywords

The physician and literary writer Silas Weir Mitchell had a long-standing interest in venom research, spanning the second half of the nineteenth century. Mitchell’s work showcases the dynamics of medical and methodological thought during a key period in the history of the biomedical sciences, just like Mead’s Mechanical Account of Poisons did for the eighteenth century. Venom research was situated at the intersection of several areas of biomedical investigation—including toxicology, physiology, medical chemistry, and therapeutics. The chapter shows how Mitchell appropriated experimental approaches from various fields to characterize both the cause and the effects of the disease caused by snake venom. The chapter also highlights the shift of emphasis in the methodology of experiments from variations of experimental procedures to comparative tests and checks. At that time, comparative experimentation was explicitly discussed both in the life sciences and in the emerging philosophy of science. However, the scientists’ discussions were driven by pragmatic concerns and thus differed significantly from systematic accounts of comparative experimentation such as Herschel’s and Mill’s philosophies of science.

Keywords:   snake venom, experimentation, methods discourse, comparisons and counterproofs, Silas Weir Mitchell, Claude Bernard, John Stuart Mill

Chapter 6 presents Fontana’s methods discourse both as a creative appropriation of a long tradition and as a product of the challenges he encountered in his own endeavors. In this chapter, Fontana’s work becomes a vantage point for the study of nineteenth-century methods discourse. I begin with Silas Weir Mitchell, whose long-standing interest in venom research spanned the second half of the nineteenth century. Today, Mitchell is perhaps best known as a novelist and poet. Historians of medicine know him as an expert on nerve injuries and as the developer of the “rest cure” for the management of nervous diseases. But clinical neurology was only one of many of Mitchell’s specialties. In biographies and obituaries, Mitchell is usually celebrated as a man of many talents—physician, educator, clinical neurologist, physiologist, poet, novelist, and medical reformer.1 For the historian of methods discourse, Mitchell’s work is of interest because it showcases the dynamics of medical and methodological thought during a key period in the history of the biomedical sciences, just like Mead’s Mechanical Account of Poisons did for the eighteenth century.

The nineteenth century has become something of a historiographical embarrassment for historians of the life sciences. Much has been written on the development of the biomedical sciences from a number of historiographical perspectives. Histories have drawn on nineteenth-century medicine, physiology, and biology to exemplify the professionalization of the sciences, the rise of the research university, the role of teaching laboratories for the advancement of medicine and biology, the formation of large, state-funded research institutions, and so on. The historiography from the 1980s and 1990s was concerned with broad developments; older histories of the biomedical sciences from this period framed the nineteenth century in terms of the “rise of scientific medicine” or the “laboratory revolution.” (p.113) More recent work in the history of the biomedical sciences has cast into doubt many of the long-standing historiographical concepts, generalizations, and grand narratives;2 even the very notion of “scientific medicine” itself has been critiqued.3 Instead, there have been calls for more localized, fine-grained, comparative studies of knowledge and practice, both in the laboratory and in the clinic.4

The study of methods discourse in mid-nineteenth-century venom research can do double duty. On the one hand, the comparison with late eighteenth-century experimental methods and methodological thought can give us a sense of the developments since the time of Fontana. On the other hand, such a study can offer a fresh perspective on mid-to late nineteenth-century biology and medicine. Venom research was situated at the intersection of several areas of biomedical investigation—including toxicology, physiology, medical chemistry, and therapeutics. Exposing continuities, resemblance, and innovation in the protocols, methodological conceptions, and commitments to experimentalism across these fields does justice to the complexities of local research environments while at the same time transcending these local contexts.

For many reasons, Mitchell’s works on snake venom are particularly suitable for an examination of the transformations of biomedical knowledge, practices, and methods discourse. His medical career path was rather typical for a member of the medical profession in the United States. His work on snakes brought together different perspectives on venom poisoning, including chemical and toxicological studies of venom as well as clinical studies of venom poisoning and of the efficacy of antidotes. Mitchell produced his main works on venom in Philadelphia around 1860 and after 1885. He commenced his project at a time when many members of the American medical community began to debate the merits and demerits of “scientific” medicine and the value of laboratories and inscription devices. Mitchell made his last contributions to venom research when new findings in bacteriology began to impinge on nineteenth-century medical thought and practice.

The Life and Career of a Medical Doctor

Laboratory research was among Mitchell’s main pursuits, but his opportunities were limited. In the mid-nineteenth century, when he was a medical student, laboratory exercises were not part of medical training. At that time, low-quality proprietary medical schools dominated the system of (p.114) medical education. Teaching was largely based on lecturing and perhaps a few dissections.5 Before the 1870s, medical men who wanted to pursue experimental research in physiology, chemistry, or toxicology were, at best, confined to small research facilities offering modest laboratory space if they did not want to work at home.

Mitchell did gain some laboratory experience while he was a student, mostly in chemistry. Mitchell’s father was a chemist, and Mitchell’s biographers note that Mitchell had been interested in chemistry from an early age.6 Because of his family relationships, the student had access to a chemical laboratory, and he could also do some research in physiology.7 After he had completed his medical training, Mitchell traveled to Europe, like other young physicians of his generation did. First he went to England, then to Paris, where he encountered Claude Bernard, the renowned French experimental physiologist, whose experimental work had drawn so many visitors to his “ghastly kitchen.”8 According to Mitchell’s most recent biographer, Mitchell’s French was so poor that he did not get much out of his visit. (In a letter to his family, Mitchell reported that he had been “greatly edified by hearing a lecture an hour long, scarce a word of which could I comprehend.”9) Nevertheless, Mitchell’s acquaintance with the French physiologist and especially with his work was formative for his entire scientific career, as we will see.

After his return to the United States, Mitchell practiced medicine in his father’s surgery, where he also pursued some research. Throughout his career, Mitchell’s access to laboratories remained limited, and even in later life, he could never devote all his time to laboratory research. His main source of income was always his surgery, and he conducted physiological experiments merely in his spare time. In his autobiography Mitchell wrote that in his early years he would spend every afternoon and evening doing research, often from 4:00 p.m. until 1:00 a.m.10 Textual traces of Mitchell’s time-consuming duties as a physician are scattered throughout his publications—in the accounts of his experiments, he repeatedly mentioned that his duties had kept him from continuing or completing projects or that he had been forced to leave an animal experiment unobserved for extended periods. One of Mitchell’s biographers notes that in the 1850s, “the front office [of his surgery] was full of patients and the back office of rattlesnakes and guinea pigs.”11 In addition, Mitchell could also make use of a modest laboratory in the Philadelphia School of Anatomy’s building.12

According to the older historiography, the development of nineteenth-century American medicine can be characterized as a steady move toward “scientific” medicine, a gradual acceptance—if slow and late compared (p.115) to Europe—of the merits of laboratory-based and experimental medical research and animal experimentation combined with the introduction of practical training as an integral part of medical education. The rise of experimental, laboratory-based research in the United States was inspired, promoted, and facilitated by the activities of many young physicians who had been to Europe—particularly to Germany—and who sought to establish similar facilities and programs in the United States.13 A number of them brought instruments home or later returned to Europe to buy laboratory equipment.14

The standard story is not wrong; it is just much too sweeping. Mitchell’s career path shows that an explicit commitment to experimentation could very well be damaging for someone wanting to be successful in mid-nineteenth-century American medicine. Mitchell spent most of his professional life in Philadelphia. In the 1860s, he encountered strong resistance from many physicians who did not support laboratory work. During the 1860s, he attempted twice to get a chair at Philadelphia, once at the University of Pennsylvania, once at Jefferson Medical College. On both occasions he lost the competition (despite ample support from renowned experimentalists) to a medical practitioner who was not an experimentalist and had better social connections to the medical and academic establishment in Philadelphia.15 “Philadelphia’s ‘lost’ physiologist” was above all a busy physician with a medical practice.16 Nevertheless, even though his attempts to become a professional physiologist remained unsuccessful, Mitchell eventually became a main player in the reforms of medical education and research at the University of Pennsylvania. In 1875, he was appointed to the board of trustees of the University of Pennsylvania, and in this capacity, he was involved in the reorganization of the medical curriculum, encouraged the shift to practical laboratory education, helped expand medical personnel, and promoted the construction of new laboratory facilities for the university.17 And, of course, he also had his literary career.

Given his many professional duties and occupations, it is astounding how much research on venom Mitchell managed to accomplish. He began his experiments in the late 1850s and continued to do venom research, on and off, until the very end of the nineteenth century. He published a number of books and articles on the anatomy, physiology, and toxicology of poisonous snakes, in particular on the chemical nature of snake venom and its effects on organs, body fluids, and tissues. The results of his first studies were published in a book-length report, entitled Researches on the Venom of the Rattlesnake: With an Investigation of the Anatomy and Physiology of the Organs Concerned. The book appeared in the series of proceedings of the (p.116) Smithsonian Institution in 1860. The complementary text, “On the Treatment of Rattlesnake Bites, with Experimental Criticisms upon the Various Remedies Now in Use,” appeared in 1861 in the Medical and Chirurgical Review and also as a separate publication in a slim volume produced by Lippincott, a Philadelphia publishing house.

During the Civil War, Mitchell did mostly clinical work, specializing in nervous diseases.18 After the war, he briefly returned to venom research and did a few experiments to clarify some issues that had arisen from his earlier work. This led to another short publication.19 But it was only around 1880 that Mitchell engaged in a new extensive project on snake venom. Edward Tyson Reichert, then a demonstrator of physiology at the University of Pennsylvania, assisted.20 The scope of the later project is considerably wider than the earlier, covering the venoms of different kinds of poisonous snakes. The results were published in 1886 as another book-length report, Researches upon the Venoms of Poisonous Serpents, coauthored by Mitchell and Reichert. The publisher was again the Smithsonian Institution. Along the way, Mitchell published a few popular essays on snake bites in magazines for general audiences such as the Atlantic Monthly and the Century Magazine. This chapter deals with Mitchell’s work from before the war.

New Audiences for Experimentalism

Michell’s two initial works on snake venom were addressed to the two major audiences in mid-nineteenth-century American medicine: those interested in “elementary research” (as experimental investigations were sometimes called) and clinicians who had an interest in effective remedies and treatment options. In his Smithsonian essay of 1860, Mitchell advanced two overall points: First, venom was a composite of components, and not all of these components were toxic. Second, venom could produce “acute” and “chronic” diseases. In acute cases, death occurred rapidly, within minutes, and in these cases, respiration and the heart became enfeebled. In secondary or chronic poisoning, death occurred only after several hours, and postmortem dissection showed changes in the blood. The slender book on the treatment of snakebite from 1861 is a treatise on therapeutics. It discusses the efficacy of antidotes, in particular “Bibron’s antidote,” a remedy for rattlesnake bites that the French zoologist Bibron was promoting.21 Both writings contain descriptions of a number of experiments.

(p.117) The reader also finds an explicit commitment to experimentalism. In the preface to the Smithsonian essay, Mitchell declared: “The conclusions arrived at in the pages of this Essay, rest alone upon experimental evidence. That in so varied and difficult a research, it may be found that I have sometimes been misled, and at others erred in the interpretation of facts, is no doubt to be anticipated. I began this work, however, without preconceived views, and throughout its prosecution I have endeavored to maintain that condition of mind which is wanted in experimentation, and that love of truth which is the parent of rational inferences.”22 In the introduction, he assured his readers that when his experimental evidence had been inconclusive, he had always admitted it—“thinking it better to state the known uncertainty thus created than to run the risk of strewing my path with errors in the garb of seeming truths.”23 In Mitchell’s treatise on therapeutics, the statement regarding the merits of experimentalist approaches in medicine is not quite as explicit. But we do find a brief commitment to rational therapeutics. The declared goal was to arrive at a rational understanding of the treatment of snakebite, which meant, to Mitchell, a quantitative, experiment-based assessment of the efficacy of treatments.

Mitchell’s version of experimentalism does not appear particularly original or novel. One would not be surprised to find such passages in an eighteenth-century text on physiological experimentation; in fact, Fontana wrote very similar things. What is relevant is not the content of Mitchell’s commitment; what is relevant is that he made it at all. Surely in the nineteenth century the value of experimentation was no longer in dispute?

Once again, it is important to remember that two of the key questions about the commitment to experimentalism are the question of the context in which the commitment was made and the audience to which it was directed. Redi conversed with fellow naturalists and with aristocratic patrons. Mead—the young Mead—sought to promote Newtonianism in a community of physicians. In Mitchell’s case, two debates are relevant: the debates within the medical community about the merits and demerits of scientific medicine and, increasingly, the debates both within the medical community and between members of the medical profession and members of the public about vivisection. The concept “scientific medicine” had different meanings for different people, it was deployed in different contexts and for different purposes, and researchers who said of themselves that they pursued “scientific” medicine did quite different things.

We already saw that Mitchell took a certain professional risk when he explicitly identified himself as an experimentalist. Although Mitchell’s (p.118) experimentalism does not sound very radical, at least in hindsight and in comparison with Fontana’s, it appears much more so if we take into account that the kind of medicine that many members of the American medical community considered properly “scientific” was observation-based medical practice. From this perspective, the promotion of experimentation must have appeared as a rather drastic move to some. In the first half of the nineteenth century, experimental research was often vehemently criticized for being speculative, mystifying, and thus unscientific. It was certainly not uncritically accepted as a sound basis for therapeutics.24

Those practitioners who advocated medical reforms and laboratory-based research did so to distinguish and distance themselves from diverse groups both within and outside the medical community. They had to defend their views within the community because several of its members did not see any practical value in laboratory-based physiology. These people argued that clinical judgment was not aided and might even be distorted if the clinician relied on the insights gained in physiological experiments.25

The commitment to experimentalism was also a provocation to those who were concerned about the use of animals in medical research. Such concerns were growing during the 1860s. Mitchell’s early essays on venom became a reference point in these debates. John Call Dalton, a physiologist at the renowned College of Physicians, presented Mitchell’s work on snake venom as an exemplary case of a new style of medical research that had displaced the old practices of seeing, touching, listening, and dissecting. In an address delivered at the New York Academy of Medicine in 1866, he commended his friend’s work for “the clearness and elegance of its style, the abundance of its material, and the precision of its results. It illustrates very distinctly the value of strictly elementary researches as a necessary preliminary to those of a more practical nature.”26 That address was, in fact, an address in defense of vivisection in response to a particularly forceful antivivisectionist attack on the medical community.27

Dalton was a great admirer of Claude Bernard; he had attended Bernard’s lectures on experimental physiology in Paris as a young man. Like Bernard, he supplemented his own physiology lectures with vivisections for the purpose of demonstration. Dalton relied on Mitchell as an ally in his battle against antivivisectionists who called for restrictions and regulations to prevent what they saw as useless and unethical cruelty in medical teaching and laboratory research.

Mitchell himself did not make strenuous efforts to defend vivisection. He gained his insights on snake venom at the cost of the lives of numerous rabbits, dogs, and pigeons, a fact that he did not hide. But unlike his (p.119) friend Dalton, who publicly, repeatedly, and expressively defended the use of live animals in physiological experimentation, he rarely explicitly addressed the issue. When he did so, in his article in the New York Medical Journal, his comments suggest that he had little patience for the sentiments of antivivisectionists and made clear that his research was not their business. He praised Dalton’s “eloquent defence of vivisection,” and he frankly stated that he took responsibility for “a large expenditure of the lives of birds, dogs and rabbits.” He was responsible to his own conscience and “to the Maker, who has endowed us with the will and the power to search into the secrets of His universe,” definitely not to those “many ignorant and well meaning persons, who have recently sought to take away from us the chief aid of the modern physiologist.”28

Mitchell’s 1861 treatise must have appeared particularly suitable for Dalton’s purpose because it illustrated how animal experimentation could be used to assess the efficacy of treatments. Nevertheless, it is one thing to advocate a program, a system, or a reform of medical practice in public lectures and addresses and to promote new programmatic goals, such as “scientific” medicine or “rational” therapeutics in order to build a community, to distinguish oneself from one’s predecessors, or to defend one’s ideals. It is quite another thing to turn these larger goals into novel kinds of approaches to biomedical research or to use these approaches in one’s research.

Dalton, at least, maintained that Mitchell’s approach to biomedical experimentation was innovative. He congratulated Mitchell on his methodological acumen. Commenting on Mitchell’s study of antidotes to rattlesnake venom, Dalton declared: “It would be difficult to find a medical treatise which should illustrate more fully than this the judicious caution and reserve which guide the physiological experimenter, and which enable him to avoid the sources of error that lie in his way. The constant employment of comparative and counterexperiments, and the frequent variation of the methods employed, indicate the care and faithfulness of the investigations, and inspire a well grounded confidence in their results.”29 We will see that Dalton’s characterization of Mitchell’s methodological ideals misses the point in a rather interesting way.

Eclectic Protocols

Mitchell stated that initially he had simply wished to evaluate the potency of Bibron’s antidote, a concoction of “five drachms of bromine, four grains of iodide of potassium, and two grains of corrosive sublimate.” He had (p.120) hoped to assess the value of the drug by procuring a few snakes, having them bite animals, and giving the antidote to the victims. But matters turned out to be less simple than he had expected. “After destroying many animals and attaining only negative results,” he embarked on a more systematic project to acquire the information that he needed: information about the nature of the venom and how it was conveyed to the victims, as well as about the precise effects it produced in them.30 The two treatises from 1860 and 1861 present the results of this endeavor.

The Smithsonian essay was written for readers who had an interest in experimentation. Mitchell’s short treatise on the treatment of rattlesnake bites addresses the readers of the Medical Chirurgical Review—an audience of practicing physicians. The Smithsonian essay referred those readers who wanted to know about rattlesnake venom “from a purely medical point of view” to the essay in the Medico-Chirurgical Review, which, in turn, referred to the Smithsonian essay those readers who were curious about the details of Mitchell’s experiments.31 In the introduction to the Smithsonian essay, Mitchell presented his project as a continuation of a research tradition stretching back to the ancients, even though he worked on rattlesnakes, not on vipers. Mitchell kept referring to Fontana’s views and experiments, and Redi, Mead, and even Celsus appear in the footnotes. But the questions he asked and the conceptual framework and protocols he used owed much more to contemporaneous questions and concerns in medical chemistry, pharmacology, and pathology than to seventeenth- and eighteenth-century investigations.

The protocols in the Smithsonian essay show that for Mitchell, the uniformity of experimental conditions became a prime concern. Mitchell had a more regular supply of resources than most of his predecessors. In the early modern period, the meat of vipers was an essential ingredient of theriac, a remedy for snakebite and various other health troubles. For their experiments, investigators often made use of the numerous vipers that had been collected for the production of theriac. Mitchell had a much smaller supply, which he obtained from various locations, mostly in the Alleghenies,32 but he kept the snakes not only to have venom readily available for his experiments at all times and also to be able to provide a regular food supply and a well-known environment for the animals. He was thus able to offer general information about the habits of rattlesnakes in captivity. And he did even more to ensure the uniformity of experimental conditions. He used known quantities of venom in his experiments, which he injected; and in the experiments on treatment, he did all experiments on dogs of (p.121) large size and used quantities that had previously been determined to be fatal.33 In the essay on therapeutics, he even turned his concern with the uniformity and stability of experimental conditions into an “experimental criticism.” Not only did he emphasize that stable and uniform experimental conditions had to be created, but also he stressed that fallacies might result if experimenters did not pay attention to this issue.

Paying attention to protocols—to the design and procedural methods of experimentation—proves useful for situating Mitchell’s work within early nineteenth-century plant and animal chemistry, pathology, and physiology of the nerves while at the same time making us aware of connections among research fields that discipline-oriented histories might miss. Mitchell investigated whether venom was a composite substance, what its proximate principles were, and whether it was possible to isolate the physiologically active principle from it. The concepts of the “proximate” or “immediate principle” and the “active principle” were key concepts in early nineteenth-century chemical analysis, particularly within pharmacology. Proximate principles are those chemical components that can be extracted from animals and plants. Mitchell’s friend Dalton defined proximate principles in his textbook of human physiology. A proximate principle is “any substance, whether simple or compound, chemically speaking, which exists, under its own form, in the animal solid or fluid, and which can be extracted by means which do not alter or destroy its chemical properties.”34 Active principles formed a subgroup of immediate principles—namely, the physiologically effective substances of plants.35

In the course of these researches, a recognizable pattern of experimentation emerged, indeed a protocol of identifying active principles through a series of steps. An exemplary case of successful isolation of an the active principle from plants—well known at the time—was François Magendie and Pierre Joseph Pelletier’s research on ipecacuanha, a plant that was known to induce vomiting. To isolate the active principle of the substance—the “emetine” or vomitive matter—the researchers studied its physical and chemical properties and its physiological effects and compared the effects with those of the substance in its original form.36 Soon after Magendie and Pelletier had announced the active principle of ipecacuanha and after they and other researchers had identified several more of these principles, these principles became known as salifiable plant bases, or “plant alkalis.” Similar investigations were carried out on strychnos plants and other plant groups. The discovery of alkaloids in plant chemistry transformed medical science in the second third of the nineteenth century.37

(p.122) In all these cases, the isolation and chemical study of the active principle is combined with animal experiments to establish the effects of the isolated chemical agent. Claude Bernard, Magendie’s student and a model for Mitchell, followed the very same steps in his famous study on curare, the arrow poison.

Mitchell’s early investigations on alkaloids fall squarely within the scope of the endeavors to isolate active principles of plants. Together with his friend, army surgeon William Hammond, he extracted the alkaloids from corroval and vao, two varieties of woorara (curare), and tested their effects on the animal organism in animal experiments. In the resulting paper, the authors explicitly refer to Pelletier’s earlier analyses of curare. They described the physical characteristics of the two substances and the extraction of the “poisonous principle” through water and alcohol. They identified the principle obtained from corroval as an alkaloid and proposed to name it “corrovalia.” Finally, they referred to experiments that showed that the substance was highly toxic.38

It is exactly this protocol that we can find in the chemical portion of Mitchell’s Smithsonian essay. The common experimental techniques for the extraction of principles were filtering or precipitating. Mitchell described how by boiling venom, decanting the liquid, filtering the coagulate, and washing it with cold water, he obtained an albuminoid substance and a fluid. Injections of each into the breasts of pigeons showed that the fluid was deadly but the coagulum innocent. Mitchell also found that treating the fluid with strong alcohol yielded a second precipitate that was highly toxic, as animal experiments established. This nitrogenous body was the active toxicological element or essential principle. In line with common practices of naming active principles—such as strychnine from strychnos, morphine from sleep-inducing opium—he named it “crotaline” (from crotalus—rattlesnake).

The second part of the Smithsonian essay deals with the diseases caused by snakebite. Here, we find two other protocols—the familiar animal experiments in which different species of animals received venom either through bites or through injections in various body parts as well as experiments that were inspired by nervous physiology.

Chapter 6 showed how the design of Fontana’s amputation experiments and vivisections embodied eighteenth-century conceptions of life and disease—not in the sense that his experiments were hypothesis-driven but in the sense that the experimental designs appear plausible in light of certain ideas about life, disease, and vital and obnoxious principles. In (p.123) the pathology portion of his book, Mitchell followed toxicological tradition when he classified snake venom as “septic or putrefacient” poison. In Matteu Orfila’s seminal work on toxicology, snake venom is one species of septic or putrefying poisons, another is “exhalations from burying-grounds, hospitals, prisons, ships, privies, marshes, putrid vegetables, and stagnant water,” and yet another is “Contagious Miasmata, emanating from pestiferous bodies, or bales of merchandize coming from a place infected with the plague.”39 The consequences of snakebite are conceptualized as disease in terms of early nineteenth-century pathological theories, and Mitchell stressed that the “natural history” of this disease, its symptoms and lesions, had to be described in detail. First and foremost, the effects of venom on blood had to be investigated. The study of blood was one of the key concerns in mid-nineteenth-century pathology. Blood was analyzed chemically and examined microscopically in both normal and diseased conditions, and experimenters hoped to modify the condition of blood in animals so as to simulate its condition in certain diseases.40 Symptoms were minutely described, and in most cases, postmortem dissections were performed to learn about lesions. Mitchell studied the symptoms and lesions caused by snake venom in several animal experiments, most often with dogs. Like Fontana, Mitchell preferred to experiment on bigger animals because symptoms and lesions were magnified, as it were. Reed-birds, for instance, were so small that they almost always died instantly when bitten by a rattlesnake; they were thus useful as indicators for the presence of venom but unsuitable for the study of its physiological effects.

The occurrence of changes in blood became the demarcation criterion between acute or primary and chronic or secondary poisoning. In acute or primary poisoning, no alteration of blood takes place. In chronic or secondary poisoning, the changes are very pronounced: coagulation, potential damage to blood disks, and fibrin disappearance in vitro with mixtures of venom and blood. All these processes were well known in contemporaneous hematology as concomitants of disease.

Mitchell’s expressed aim was to illustrate both “constant” and “exceptional” lesions accompanying the disease of venom poisoning. He presented his results in the form of tables, which list essential information about each trial—which body part was wounded, time of death, symptoms such as convulsions, internal lesions, and—last, and most important for the characterization of the disease produced by the venom—the state of the blood in each trial (“loosely coagulated,” “chiefly uncoagulated,” and so on). To the reader, the table highlights that there is no constancy in the (p.124) lesions except that the blood is affected. The last of the columns includes everything from “blood perfectly fluid” to “coagulated well,” for example. The table related to the poisoning of rabbits contains so much information that it is too big to be squeezed onto a single printed page. It is split in two parts, a table of symptoms and a table of lesions. Table I lists the twitching, jerking, gritting of teeth, the convulsions and the labored breathing. Table II describes the appearance of the inner organs and the character of the blood. Again the reader is left with the impression that the only general conclusion that can be drawn is that based on the information provided, no generalization about the venom disease can be made.

Although the pathological perspective dominates the second part of Mitchell’s treatise, there are a number of experiments on physiological effects—namely, the study of venom on the sensory and motor nerves of frogs. The source of inspiration is obvious: Following Galvani’s discovery of animal electricity, numerous experimenters repeated Galvani’s experiments to explore muscle and nerve functions.41 Mitchell investigated the twitching of frog muscles, using venom instead of galvanic stimuli. Mitchell did not comment on the design; indeed, he probably did not have to. He merely informed the reader that the frog was “prepared as if for use for a galvanoscope,” which must have been clear enough information for the mid-nineteenth-century physiologist.42

The purpose of these experiments was not to produce and study a disease. Rather, the experiments were designed to study the effects on specific body systems (such as nerves). Experimental changes had to be such that the body system of interest was isolated, stimulated, and the effects (such as twitches) were recorded.

The section does not quite fit with the rest of Mitchell’s project—no diseases, symptoms, or lesions are described, no substantial conclusions drawn from the experiments. Precisely for this reason, the section is telling. It shows that mid-nineteenth-century biomedical experimenters could (and did) draw on a common stock of protocols. Tracing protocols across contexts and time periods helps in appreciating what is novel, what is part of a long tradition, and how different scientific fields are connected.

Comparisons and Counterproofs

The recurrent theme of late eighteenth-century methods discourse was variation, or “diversification.” Mitchell, by contrast, only occasionally mentioned (p.125) variations of experimental conditions. This certainly does not mean that he did not care to perform variations. Dalton for one commended him on “frequent variation of methods employed.” But Mitchell himself did not discuss this practice, at least not nearly as much as the late eighteenth-century experimenters did. Only once or twice did he explicitly note that the repetition of an experiment with some variations in the setting was a crucial strategy for proper experimentation, and when he did so, he sounded like an echo of Fontana. Having described a particularly intricate experimental design, he noted: “it is still desirable that these experiments should be repeated, with every possible modification; since, as I have endeavoured to show, this, like all other portions of our subject, is girt about with such difficulties as may well baffle the most careful.”43 The methodological term that stands out both in the Smithsonian essay and in Mitchell’s essay on the treatment of snakebite is the term test or check. The word test is used in several ways, depending on the context. “Test” can simply mean “examine further,” as in the phrase “the irritability of the motor nerves in the sciatic trunk was next tested.” In chemical experimentation, “test” means an indicator for a chemical substance. Even small birds can be used as “tests”—as indicators—for the presence of venom. The term test can also be used in the sense of “probe.” “To probe” or “to test” means to determine the existence or quality of something—for example, the acidity of a solution. Some common procedures for doing so were described in chemistry handbooks.

From the perspective of the history of methods discourse, the most intriguing instance of “test” or “check” is the test that involves comparative experimentation. For example, when Mitchell determined the toxic effects of a boiled mix of venom and water or an otherwise chemically altered venom, he secured a small quantity of pure venom as a “toxicological test” of the activity of the pure venom against which the toxicity of the mixture was determined.44 Sometimes he also referred to such a procedure as a “check experiment.” Conversely, the results of experiments with combinations of venom and chemicals were “checked or tested” by giving the chemical substance alone to an animal. In this way, one could establish whether a strong reagent alone was fatal. When Mitchell studied the effect of a mixture of venom and alcohol on a pigeon, he noted that a “check experiment” had been performed to see what happened if the pigeon was injected only with alcohol.45 When Mitchell investigated the effect of venom on muscles, he punctured exposed muscles with dry clean fangs whose ducts had been stopped with wax and compared the time and (p.126) intensity of the twitching with the effects of an injection of venom through the fangs.46

Mitchell made the performance of a comparative experiment a condition of proper experimental procedure. He did so in a critical comment to study some recent experiments on the effect of venom on plants, a description of which he had found in the St. Louis Medical and Surgical Journal. The author who was the target of Mitchell’s criticism had used a lancet to inoculate healthy vegetable plants with snake venom. The plants were found withered the next day. Mitchell pointed out that the methodology was lacking; indeed, he found the accounts in the Medical and Surgical Journal “so very limited, and so wanting in statement of details, that it is difficult to accord them any great value as scientific evidence.”47 To be able to assess the validity of the results of experiments other investigators had performed, readers had “a right to demand every possible knowledge as to the temperature and season, the size of the plants, the amount of venom employed, and the effect of wounding similar plants to the same extent, but without the use of the venom.”48

Mitchell’s emphasis on comparisons did not remain unnoticed. Dalton specifically mentioned Mitchell’s “constant employment of comparative and counterexperiments.” We have seen in earlier chapters that the practice of comparative experimentation had long been common in the experimental sciences and that there are even a number of premodern precedents for this practice. Fontana made it a maxim to perform comparative experiments to assess the validity of experimental results. However, only in the first half of the nineteenth century do we find more explicit and critical analyses of the structure of these comparative experiments. At that time, comparative experimentation was explicitly conceptualized in books on the logic of science (or natural philosophy). Here, the model was physical experimentation. In John Herschel’s Preliminary Discourse of the Study of Natural Philosophy, for example, comparative experimentation is introduced in Baconian terms as an example of “crucial experiments.” Like Bacon, Herschel ascribed special status to these kinds of experiments. In addition, he had quite concrete things to say about their structure, and he also offered a general characterization: “We make an experiment of the crucial kind when we form combinations, and put into action causes from which some particular one shall be deliberately excluded, and some other purposedly admitted; and by agreement or disagreement of the resulting phenomena with those of the class under examination, we decide our judgment.”49 Herschel then proceeded to discuss in detail (p.127) the rules that should guide the search for causes through comparative experimentation.

A few years later, John Stuart Mill introduced the “method of difference” as the very mark of experimentation. Mill found inspiration in Herschel’s methodological discussion as well as in another renowned treatise on method, Auguste Comte’s Cours de philosophie positive (1830–42).50 Both Comte and Mill characterized physical experimentation—the ideal type of experimentation—as an act of placing an object in definite artificial conditions. (Observation, by contrast, is a noninterventionist, passive process, as Herschel also noted.) The method of difference is a comparative method, whereby the experimenter compares two states of affairs: the preexisting state in which the phenomenon of interest is absent and the new situation in which that phenomenon has been introduced. If an effect occurs only in the second situation, then one can conclude that the phenomenon that the experimenter introduced is the cause of the effect in question.

In the most basic sense, the method of difference thus involves the comparison of an artificial situation with the natural course of things. In actual experimental inquiries, the comparison will usually be between two artificial situations, in one of which the phenomenon of interest is present and in the other of which it is absent. In any case, it is critical for the successful application of the method of difference that all conditions of the initial state be fully known to the experimenter. The method of difference is definitive; it is, according to Mill, the only method by which one can ever “arrive with certainty” at knowledge about causes.51

Mitchell’s and Dalton’s comments on comparative experimentation, already quoted, resonates with these more abstract discussions of the methodology of experimentation. Yet we should not jump to the conclusion that experimenters in the life science “applied” Mill’s methods. Dalton, for one, was likely drawing on another source: Claude Bernard.

Bernard, too, had something to say about the structure of comparative experimentation, but he gave the issue a new twist. He introduced the terms comparative experiment and counterproof as technical terms, and he explicitly contrasted the two. He insisted that comparative and counterproof were different things—the first relevant for physiology, the second for physics.

Bernard’s 1865 monograph Introduction to the Study of Experimental Medicine is the sum total of Bernard’s reflections on the proper methods of physiological experimentation. In it, Bernard outlined a methodology of physiological experimentation that carved out a special niche for (p.128) comparative experiments in physiology. Bernard acknowledged that experimentation in biology was less definitive than experimentation in physics. In this he followed his compatriot Comte as well as the Englishman Mill. Bernard agreed with Mill about the importance of the “method of difference” for physics, but he insisted that the method of difference was rarely applicable in physiology, because the experimenter was never in a situation in which all the experimental conditions and effects were fully known. In this respect Bernard was in tune with Comte, who maintained that biological phenomena were so complicated and complex that they offered “almost insurmountable impediments to any extensive and prolific application of such a procedure [experimentation] in biology.”52

Comte suggested two ways in which experiments in biology should proceed. The artificial phenomenon could be introduced either into the environment of the organism or into the organism itself. The second option was highly problematic and not very informative, because the “natural sympathy” of the organs, their harmony, would obstruct experimental practice. Comte favored the first kind of experimentation, which made experimenters “better able to circumscribe, with scientific precision, the artificial perturbation we produce; we can control the action upon the organism, so that the general disturbance of the system may affect the organism very slightly; and we can suspend the process at pleasure, so as to allow the restoration of the normal state before the organism has undergone any irreparable change.”53 Bernard, however, was more confident about the power of comparative experimentation. Even though he agreed that strictly speaking the method of difference could not be applied to physiology, experimentation in the life sciences could lead to more definite results than Comte had assumed. The hallmark for proper procedure is the “comparative experiment.”

Bernard’s concept of comparative experimentation in physiology was his answer to the complexity of life and the intricacy of the living organism he encountered as experimenter. In Bernard’s methodological discussion, a conceptual tool specifically for the practical purposes of experimental physiology emerged.54 Bernard explicitly contrasted the comparative experiment with another, more definite kind of check or test: the “counterproof.” The counterproof is connected to experimental reasoning in physics. It is the successful application of the “method of difference.” The method of comparative experimentation is a pragmatic counterpart of the method of difference as it were, a method that takes into account that life, living organisms, and their environments are too complex to be fully understood by the experimenter.55

(p.129) Like many other medical men, and in stark contrast to advocates of Newtonian medicine, Bernard insisted that methodological ideas from physics could not simply be transferred to the life sciences and that biomedical experimentation was profoundly different from physical experimentation. Experimenters could never make rigorous experiments on living animals “if we necessarily had to define all the other changes we might cause in the organism on which we were operating. But fortunately it is enough for us completely to isolate the one phenomenon on which our studies are brought to bear, separating it by means of comparative experimentation from all surrounding complications.” Comparative experimentation reaches this goal by adding “to a similar organism, used for comparison, all our experimental changes save one, the very one which we intend to disengage.” Suppose an experimenter wished to study the result of section of a deep-seated organ. Getting to that organ would require injuring other surrounding organs. What is the effect of the section itself, and what is collateral damage? To avoid confusion about causes and effects, the experimenter must perform the same operation on another animal without actually performing the section. “Comparative experimentation in experimental medicine,” Bernard pronounced, “is an absolute and general rule applicable to all kinds of investigation, whether we wish to learn the effects of various agents influencing the bodily economy or to verify the physiological rôle of various parts of the body by experiments in vivisection.”56

Bernard even insisted that because of the variability of experimental animals, comparative experiments must be performed on one and the same animal, whenever possible. At this point, it is obvious that the Introduction to the Study of Experimental Medicine was the product of Bernard’s reflections on his own experiences with physiological inquiries, because Bernard’s toxicological work contains some illustrative examples of the practice of comparative experimentation on one and the same animal. To investigate the influence of curare on the irritability of muscles, Bernard experimented on frogs. He found the irritability of frogs to be so variable that it was not illuminating to conduct comparative experiments on two different frogs. The comparison had to be performed on one and the same animal. Bernard described in text and image how the frog had to be prepared in such a way that only one of its hind legs would be affected by curare. In this arrangement, the irritability of the “normal” and the poisoned leg could be directly compared.57

The divergence from Mill’s methods is crucial. Bernard did not assume that in actual physiological experimentation, all causal factors are (p.130) knowable and can be isolated and individually manipulated, nor that the experimenter has full power over the experimental setting. In other words, the notion of comparative experimentation is a retreat from Mill’s ideal. As is well known, Bernard was a determinist at heart, and he firmly believed that organisms were governed by general laws.58 Still, the introduction of the concept of comparative experimentation is an explicit acknowledgement that in practice, ideal experimental conditions could only be approximated. Comparative experimentation was seen as a realistic workable counterpart to Mill’s ideal, not an elaboration of it. Mill’s methodology could not address the most pressing problems of scientific experimentation in the life sciences—the complexity of living things. Bernard tried to cope with what Ronald Fisher would later call “the [experimenter’s] anxiety of considering and estimating the magnitude of the innumerable causes by which his data may be disturbed.”59

It is hard to say whether Dalton was aware of, and whether Mitchell could have been aware of, the subtleties of Bernard’s position. Mitchell, of course, knew Bernard’s physiological writings, especially his work on toxicology and the studies on curare. Bernard’s Introduction to the Study of Experimental Medicine, however, appeared a few years after Mitchell had completed his main project, just before Dalton gave his address in defense of vivisection. Mitchell did not make a distinction between “counterproofs” and “comparative experiments.” His tests or checks involve a comparison along the lines of the method of difference, and we have seen how important it was for Mitchell to obtain uniform and stable experimental conditions.

Dalton’s “Bernardian” reading of Mitchell’s methodology as “constant employment of comparative and counterexperiments” is not entirely appropriate (if we read “counterexperiment” as “counterproof”). Although Mitchell’s methodology favored comparative experimentation, it did not reflect the methodological distinction that Bernard made between comparative experiments and counterproof. However, the important point is not whether Dalton interpreted Mitchell correctly or whether Mitchell had read Bernard correctly but rather that there was now an ongoing discussion about the very structure of proper experimental procedures. This discussion was not completely detached from scientific pursuits, but the more abstract reflections about experimental practice were presented in venues other than scientific articles and proceedings. Herschel’s Preliminary Discourse of the Study of Natural Philosophy, Comte’s Cours de philosophie positive, Mill’s System of Logic, and even Bernard’s Introduction (p.131) to the Study of Experimental Medicine are not—at least not primarily—outlets for the presentation of research outcomes. They are primarily (methodo)logical treatises. In these discussions, the difference between the practice of identifying causes in complex, complicated real-life experimentation and the structure of causal reasoning in ideal experimental situations came to the fore. The experimenters in the life sciences tried to develop strategies for the former, whereas the authors of methods treatises concentrated on the latter.

Experimental Criticisms

Apart from the general commitment to experimentalism, the Smithsonian essay contained very little explicit methodological discussion. In the essay on therapeutics, by contrast, methodological issues are explicitly addressed, as the full title of the work indicates: On the Treatment of Rattlesnake Bites, with Experimental Criticisms upon the Various Remedies Now in Use. Mitchell’s notion of “experimental criticism” is ambiguous, however. It means both the experiment-based critique of common beliefs about treatment options and the critique of experiments themselves. The reader finds detailed discussions of the efficacy of two chemical agents that were used for the treatment of snakebite: iodine, which was promoted by the Chicago physician David Brainard, and Bibron’s antidote. The efficacy of both agents had been tried in experiments before, but according to Mitchell, these experiments had been poorly designed.

The practical criticism of experiments on antidotes involved a discussion of two “fallacies of experimentation”: “1. Fallacies in regard to the use of antidotes of all kinds, arising from want of exact knowledge as to the secretion of venom, and the mode in which the serpent uses its fangs and ejects the poison. 2. Fallacies as to antidotes, arising from want of information on the natural history of the disease caused by the venom.”60 The experimental criticism as Mitchell presented it is an intriguing conglomerate of factual and methodological critique of snake venom research. In part, Mitchell chided his fellow researchers because they did not correctly understand basic facts about snakes. Nor did they understand the mechanisms of different kinds of antidotes. This lack of understanding also led to badly designed experiments—experiments with indeterminate quantities of venom, for example. The efficacy of antidotes could only be assessed if similar cases were compared, and this condition was not easy (p.132) to ensure. The venoms from snakes of different age, size, or vigor might not be alike. And even if two snakes were alike in these respects, and even if the amount of venom contained in their fangs were the same, it did not mean that their bites were alike, too. In fact, the mechanisms of the bite differed so much that “the danger of the bite is utterly unequal.”61

The most important experimental criticism had to do with proper accounting. In many known cases of snakebite, the disease caused by venom was, in fact, not fatal for human victims. Like the proverbial cold medicine, which is guaranteed to cure a cold in seven days, an antidote to snake venom might be much less potent than advertised. To assess the efficacy of a particular treatment, it was not enough simply to assume that snake bites are always fatal and then to estimate how successful an antidote was by counting how many of a group of treated individuals died. Instead, one must investigate the natural history of the venom-induced disease, including the question of how many individuals actually died from it.

Mitchell’s criticisms are particularly interesting in view of the discussions in the first half of the nineteenth century about the value of numbers, statistics, and quantification in medicine.62 In the medical community more generally, this discussion intensified in the early nineteenth century as a debate about the merits and demerits of the so-called numerical method that the French clinician Pierre Charles Alexandre Louis had developed. The numerical method was a quantitative tool for the systematic comparison of therapeutic outcomes in groups of patients. It involved collecting instances for the success and failure of a particular treatment.63

Louis compared groups of patients who all had the same disease—angina tonsillitis or pneumonitis, for example. These groups of patients were bled on different days, the effect of the treatment was recorded, and the average duration of the disease for the different groups of patients was calculated. There were three problems that Louis hoped to address in this way. First, the conditions for treatment and therapeutic assessment were complex and not always completely uniform. Second, strictly speaking, no two patients were alike. They differed on features such as the severity of the disease, age, strength, stature, and so forth. Third, there was the possibility of error of judgment on the side of the therapist—it was extremely challenging for the observer to make precise judgments about the time of the onset of the disease, its termination, or its severity. Drawing on Laplace’s work on probability, Louis insisted that all these issues could be addressed by comparing the responses to treatment of large groups. He reasoned that in large groups, the similarity of conditions “will necessarily (p.133) be met with, and all things being equal, except the treatment, the conclusion will be rigorous.” In the assessment of groups, “the errors, (which are inevitable,) being the same in two groups of patients subjected to different treatment, mutually compensate each other, and they may be disregarded without sensibly affecting the exactness of the results.”64

The reasoning underlying here is different from the reasoning that motivated many variations of experimental trials. Notably, it is directly opposed to Fontana’s approach to experimentation. As we have seen, Fontana assumed that through systematic variations of experimental conditions it was possible to identify all the circumstances that potentially affected experimentation. Louis, by contrast, called for the treatment of large groups, because he assumed that these factors could not be reliably identified.

The fate of the numerical method is well known. Many members of the nineteenth-century medical community were rather critical of Louis’s approach and of statistical approaches more generally. Bernard in particular was very much opposed to statistics, and his critique of the numerical method was biting. In the Introduction to the Study of Experimental Medicine, Bernard reiterated some of the criticisms against the numerical method that Louis himself had already anticipated in his treatise on bloodletting. The first requirement for the proper use of statistics was that “the facts treated shall be reduced to comparable units.”65 But in clinical contexts, this requirement could not be met. The records were not reliable, diagnoses were obscure, the causes of death were often carelessly recorded, and so on. Because there was too much variety among the individual patients, averages were meaningless. Bernard also abolished statistics in experimental physiology, drawing attention to a controversy that his own research had helped resolve. Experimenting on the spinal nerve, some experimenters had found that the anterior spinal roots were insensitive but others that they were sensitive, and Bernard asked: “Should we therefore have counted the positive and negative cases and said: the law is that anterior roots are sensitive, for instance, 25 times out of a 100? Or should we have admitted, according to the theory called the law of large numbers, that in an immense number of experiments we should find the roots equally often sensitive and insensitive?” Of course not. Such statistics would be “ridiculous.” The proper scientific way to deal with the case would be to establish the exact conditions in which spinal roots are sensitive and insensitive.66 Statistics was wanting, because statistical approaches did not provide any insight into causes. The correct approach to physiological inquiry was the experiment-based search (p.134) for causes, according to Bernard—and we already saw how he thought he could address the problem of individuality through his conception of comparative experimentation.

Even those members of the medical community who welcomed quantitative approaches to the study of disease were quick to criticize Louis, because he justified his method along the lines of the law of large numbers, and the populations he examined in his trials were rather small. Others criticized the advocates of the numerical method because it led the physician away from the individual sick patient. Yet others had qualms about the method itself, like Bernard did: it was based on the wrong assumption that all patients were alike. As William Coleman has shown, there were a few attempts in the mid-nineteenth century to improve on Louis’s approach and to introduce statistical tools that were more appropriate to the very small numbers of subjects that were used in therapeutic trials (as well as in physiology). But the medical community at large did not welcome these tools. Therapeutic trials on groups of patients continued to be pursued, but there was little methodological discussion and reflection on these trials. The discussion intensified again only around 1900, and it was then that statistical tools came to be accepted in the medical community.67

Mitchell’s essay on treatments of snakebite is remarkable because it outlines the conditions for adequate tests of the efficacy of antidotes along the lines of the numerical method. The “experimental criticisms” Mitchell put forward in the 1861 essay on the treatment of snakebite resonate with some of the issues Louis discussed. Mitchell’s conceptualization of experimental animals as “diseased” made it possible for him to frame the method for the assessment of animal experiments in those terms. We have seen how concerned Mitchell was with uniformity and stability of experimental conditions. At the same time, he emphasized the individuality of the “patients”—the snakebite victims—he considered in his experiments. This becomes most obvious in the 1868 study on rattlesnake bites, which supplemented the earlier essays. Mitchell remarked: “The puzzling factor of individuality perpetually comes into the equation with elements of doubt, so that it is only by multiplying results that we can reach the requisite amount of assurance that in a large given number of animals the individual cases of unusual resistance are not likely to interfere with our conclusions.”68 For Mitchell, the reason why many animals needed to be treated was that animals were individuals; they all reacted slightly differently to the treatment with venom. In this sense, they were like sick patients receiving treatments.

(p.135) Unlike Bernard, Mitchell assumed that for the correct assessment of the power of an antidote and for the evaluation of the success of treatments, some application of statistics was required. In particular, the mortality rate of snakebite victims must be known. One reason why some of the experiments in the Smithsonian essay were so remarkable was that they showed that some species of animals were more resilient than others. Dogs, for instance, were much less likely to die than were rabbits and pigeons, and in half the experiments on the effect of rattlesnake venom on dogs that Mitchell reported, the bite victims recovered. (The survivors did not necessarily escape their fate, though: The large spaniel who was recovering from a bite in its shoulder “was so well on the ninth day, that it was used for another purpose.”69) Contrary to popular opinion, it was also not true that rattlesnake bites were always fatal for humans. Referring to another table in the Smithsonian essay, which showed that several snakebite victims had recovered after treatments with oil, alcohol, iodine, and other substances, Mitchell commented drily: “either all treatment […] is successful, or else […] the greater part of the cases must have survived under any form of medication.”70 What seemed to be a successful treatment might as well be a case of recovery by natural causes. In any event, “[t]he mere fact of their surviving can assuredly be no test of the value of a plan or treatment.”71 Because there were no comprehensive statistics about the fatality of rattlesnake bites, it was not possible to make any concrete assessments of the efficacy of treatments.

The results of Mitchell’s own experiments with Bibron’s antidote were discouraging: Of nine canine snakebite victims that were treated with the drug, only two survived. Given that roughly every second victim survived without any treatment, this number is not too impressive. Experiments with other agents were equally disappointing. If done properly, these experiments showed that those treatments were in fact ineffective.72

Some New Arrangements in the Narrative

Fontana composed his celebrated treatise on viper venom in the late eighteenth century. Mitchell put together his reports about eighty years later. We have already seen about the changes in the content of methods discourse, especially the quite fundamental changes in the protocols and the shift of emphasis from variations to “checks” in the methodology. Even the commitment to experimentalism, although quite similar in its wording, (p.136) had new significance in the context in which Mitchell made it. One might also expect quite a bit of change in the organization of experimental reports between the late eighteenth and the nineteenth centuries. Indeed, historians of scientific writing have argued that the changes in this period were particularly profound. They find in the second half of the nineteenth century the roots of the modern, modular form of scientific writing—that is, the familiar division into the sections “Introduction,” “Methods,” “Results,” and “Discussion.” These historians maintain that in the course of the nineteenth century, methodological reflections disappeared from experimental reports and that the reports (especially the articles in scientific journals) became increasingly less reflexive and more standardized. The alleged decrease in reflexivity and the increase in standardization are taken as indications that methodological issues in the experimental sciences were largely settled.73

This view strikes me as problematic and misleading in several respects. Mitchell’s essays exemplify a transitional stage—they do exhibit some new features that we recognize in hindsight as anticipating organizational elements of later scientific writings but they were in many ways quite traditional. It is obviously not the case that methodological issues were largely settled. There were quite intense discussions in the mid-nineteenth century about all sorts of methodological issues—about the numerical method and quantification, about statistics, about the structure and epistemic force of comparative experimentation, and so on. Even though there might have been fewer discussions of methodological issues within experimental reports, the methodology of experimentation clearly was still a topic of concern.

At least for the most part, accounts of experiments were still organized sequentially. Protocols were described along the way, not in separate methods sections. Like Fontana, Mitchell combined narrative and methodological statements to form an argument. For instance, like Fontana, Mitchell described how particular experimental settings were gradually improved to make the findings more secure. One such sequence of trials explored the influence of heat on the destructive power of venom. In these experiments, the venom was heated to successively higher temperatures and then injected into the breasts of small birds. The report includes a table showing the results of a series of ten experiments. Death occurred after longer and longer times, and the bird that received venom heated to 212 °F survived the injection. The table thus suggests that the venom gradually lost its power when heated and had become completely (p.137) inactive at 212 °F, and Mitchell stated this.74 In the next paragraph, he declared that his conclusion had been mistaken. Only then did he state that he had re-examined the issue after some time. The new experiments had demonstrated that the results as they are shown in the table were misleading because they falsely suggested that heated venom was less dangerous than venom at room temperature. He went on to describe the causes of the error into which he had fallen: He reminded his readers that boiling caused coagulation of a part of the venom and that the active portion of the venom was in the fluid, not in the coagulant. He had been forced to work with very small quantities of venom, which meant that the amount of fluid venom was minute. During the boiling process, most of that fluid would cling to the test tube and would thus not be injected. This was the reason why at higher temperatures death occurred more slowly or not at all. The remedy was straightforward: The experiments had to be done with larger quantities of venom. Indeed, in the second series of experiments, all birds died “with the usual symptoms.”75 In sequences like these, the order of presentation matters for the argument. The narrative describes the gradual stabilization of an experimental arrangement, culminating in the specification of a causal relation (or, as in this case, the absence of one). The point of the description of the experiments resulting in the misleading table is not simply that Mitchell was an honest man, honest enough even to admit that some of his experiments had failed. Rather, by showing how one could explain what happened when small quantities of venom were boiled, Mitchell strengthened his own position. The outcome of the failed experiment made perfect sense if it was considered in light of his idea that venom was a composite of a fluid and a precipitating part.

This manner of writing is quite similar to late eighteenth-century experimental reports. What is different is that the flow of the narrative is occasionally broken up and that Mitchell did not leave the reader in suspense, at least not to the same extent as Fontana did. Both of these new arrangements are indicative of a move away from the main goal that Fontana pursued in his writing—to demonstrate the discoverability of his findings to the reader. The new arrangements indicate a move toward making it easier for the reader to grasp the significance of the findings. The data Mitchell obtained in his experiments are sometimes (not always) presented in tables, which are typographically separated from the main text.

In a table, descriptions of actions and findings are necessarily terse and succinct and are often represented by a number, space in the columns being limited. Mitchell’s table has seven columns. The first gives the number (p.138) of the trial. The second states the number of fang marks: one or two. The third lists body parts bitten: Thigh. Breast. Back. Leg. The fourth column presents the “duration of life from the time of the bite,” times ranging from two hours to nine hours, ten minutes. The symptoms and lesions are also just briefly indicated. The fifth through seventh columns contain pithy characterizations of visible symptoms and alterations of organs and body fluids.

Mitchell’s tables could not remove the uncertainty about what overall conclusions might be drawn from the empirical findings—and, of course, tables are not a nineteenth-century invention. But the introduction of tables had a quite profound effect on the organization of Mitchell’s argument, as the emphasis shifted from describing the way in which data were produced to the synoptic presentation of evidence. This benefits the reader. Producing and filling in the table forced the author to be systematic and comprehensive and to abstract from the actual chain of events. Information presented in tabular form can be taken in at a glance; comparisons between trial outcomes are quick and easy to make. The format of the table, the spatial limitations set by the rows and columns necessitated the introduction of salient categories (“locality of the bite,” “state of blood”) and descriptive concepts (“uncoagulated,” “loosely coagulated”). In this sense, the presentation of relevant information in tabular form is a significant divergence from the narrative format of the investigative journey that we find in other parts of the Smithsonian essay.

In contrast, Mitchell’s 1868 essay on the toxicology of rattlesnake venom, the supplement to the earlier essays, presents a narrative consisting of a string of linked experiments performed to answer a particular research question. Mitchell asked: Why is it that venom is not poisonous when ingested? Why does it not act on the mucous surfaces of the stomach? The discussion begins with a hypothesis—either the venom is altered by the gastric juices, or it is incapable of osmosis. The narrative covers a series of experiment to determine which of the alternatives is correct. The story is driven by inconclusive results that needed to be clarified and by new questions that these experiments opened up. Mitchell held his readers’ interest through remarks such as “To relieve myself of doubt, I made a second set of experiments …” or “I resolved my difficulties by the following experiment. …”76 The readers can follow along and are drawn into the story by Mitchell’s account of inconclusive outcomes, open questions, false leads, new leads, and failed trials.

This report closely resembles the eighteenth-century accounts of investigative (p.139) journeys. Mitchell’s readers also learned that even though the question was clear, there was no distinct, decisive experimentum crucis that could unmistakably identify one of the two alternatives as correct and the other as false.77 Much intricate and challenging experimentation was needed for the experimenter to reach the point at which such a decision could be made with some confidence.

Notes:

(1.) On Mitchell’s life and work in the context of the wider American culture, see, e.g., D. J. Canale, “Civil War Medicine from the Perspective of S. Weir Mitchell’s ‘The Case of George Dedlow,’” Journal of the History of the Neurosciences 11 (2002): 11–18; Laura Otis, Membranes: Metaphors of Invasion in Nineteenth-Century Literature, Science and Politics (Baltimore, MD: Johns Hopkins University Press, 1999); Christopher Goetz, “Jean Martin Charcot and Silas Weir Mitchell,” Neurology 48 (1997): 1128–32; Nancy Cervetti, “S. Weir Mitchell and His Snakes: Unraveling the ‘United Web and Woof of Popular and Scientific Beliefs,’” Journal of Medical Humanities 28 (2007): 119–33; and Nancy Cervetti, S. Weir Mitchell, 1829–1914: Philadelphia’s Literary Physician (University Park: Pennsylvania State University, 2012). On the institutional conditions of Mitchell’s career, see W. Bruce Fye, “S. Weir Mitchell, Philadelphia’s ‘Lost’ Physiologist,” Bulletin of the History of Medicine 57 (1983): 188–202.

(2.) See Warner, “Ideals of Science and Their Discontents.” See also Jardine (in turn drawing on Walter Pagel) for the “plethora of programmes for making medicine scientific”: Jardine, “The Laboratory Revolution in Medicine,” 305.

(3.) scientific medicineRonald L. Numbers, “Science and Medicine,” in Wrestling with (p.253) Nature: From Omens to Science, ed. Peter Harrison, Ronald L. Numbers, and Michael H. Shank (Chicago: University of Chicago Press, 2011), 214–15.

(5.) S. Weir Mitchell, Memoir of John Call Dalton, 1825–1889 (National Academy, 1890), 179–80.

(6.) Anna Robeson Burr, Weir Mitchell—His Life and Letters (New York: Duffield & Co, 1929), 28–29.

(7.) W. Bruce Fye, The Development of American Physiology: Scientific Medicine in the Nineteenth Century (Baltimore, MD: Johns Hopkins University Press, 1987), 57.

(8.) Claude Bernard, An Introduction to the Study of Experimental Medicine (New York: Dover Publications, 1957; 1865), 15. Several of those physicians who later played leading roles in America’s medical community went to Claude Bernard’s laboratory in Paris; see John Harley Warner, Against the Spirit of System: The French Impulse in Nineteenth-Century American Medicine (Princeton, NJ: Princeton University Press, 1998). Mitchell’s friend Dalton attended Bernard’s lectures on experimental physiology.

(11.) Ibid., 97.

(13.) William F. Bynum, Science and the Practice of Medicine in the Nineteenth Century (Cambridge, UK: Cambridge University Press, 1994).

(14.) Robert Frank, “American Physiologists in German Laboratories, 1865–1914,” in Physiology in the American Context, 1850–1940, ed. Gerald Geison (Bethesda, MD: American Physiological Society, 1987), 11–46.

(15.) For Mitchell’s failed attempts to obtain a chair in physiology, see Fye, The Development of American Physiology, 66–67, 68–73; and Cervetti, S. Weir Mitchell, 70–71, 93–95.

(16.) Historian Bruce Fye coined this experession; see Fye, “S. Weir Mitchell, Philadelphia’s ‘Lost’ Physiologist.”

(18.) On Mitchell’s clinical work and literary writings during the civil war, see, e.g., Canale, “Civil War Medicine.” The horrifying short story “The Case of (p.254) George Dedlow” is an impressive example of how Mitchell incorporated contemporary medical thought in literary projects.

(19.) S. Weir Mitchell, “Experimental Contributions to the Toxicology of Rattle-Snake Venom,” The New York Medical Journal (1868): 289–322.

(20.) Reichert became the chair of physiology at the University of Pennsylvania in the mid-1880s, with Mitchell’s support; see Fye, The Development of American Physiology, 88–89.

(21.) S. Weir Mitchell, On the Treatment of Rattlesnake Bites, with Experimental Criticisms Upon the Various Remedies Now in Use (Philadelphia, PA: Lippincott & Co., 1861).

(22.) S. Weir Mitchell, Researches on the Venom of the Rattlesnake (Philadelphia, PA: Smithsonian Institution, 1860), iii–iv.

(23.) Ibid., 1.

(25.) Gerald Geison, “Divided We Stand: Physiologists and Clinicians in the American Context,” in The Therapeutic Revolution: Essays in the Social History of American Medicine, ed. M. J. Vogel and Charles E. Rosenberg (Philadelphia: University of Pennsylvania Press, 1979), 67–90. In 1871, for instance, the Harvard surgeon Henry J. Bigelow stated the following in an address on medical education: “In an age of science, like the present, there is more danger that the average medical student will be drawn from what is practical, useful, and even essential, by the well-meant enthusiasm of the votaries of less applicable science.” Bigelow was not at all enthusiastic about experimental physiology, which “leads away from broad and safer therapeutic views, and toward a local and exclusive action of chemistry and cells,—uncertain grounds for students, for whom the result of large and well-attested medical experience is here the safest teaching, and a habit of mind leading to experiments on patients the most questionable”; quoted after Fye, The Development of American Physiology, 107, 108. See also Christopher Lawrence, “Incommunicable Knowledge: Science, Technology and the Clinical Art in Britain 1850–1914,” Journal of Contemporary History 20 (1985): 503–20.

(26.) John Call Dalton, Vivisection; What It Is, and What It Has Accomplished (New York: Baillière brothers, 1867), 35.

(32.) Mitchell acknowledged the aid of the Smithsonian Institution in procuring the snakes.

(33.) Mitchell, On the Treatment of Rattlesnake Bites, 39. In the Smithsonian essay, there is no evidence that he attempted to select experimental animals that (p.255) were alike—a dog was a dog, a rabbit was a rabbit. In part, this may have been simply a practical issue of availability or cost, because Mitchell did emphasize in his reports that differences in age or weight might be important (for dogs more so than for rabbits or pigeons) and should be noted in the experimental report.

(34.) John Call Dalton, Treatise on Human Physiology, Designed for the Use of Students and Practitioners of Medicine (Philadelphia, PA: Blanchard and Lea, 1859), 31.

(35.) John E. Lesch, “Conceptual Change in an Empirical Science: The Discovery of the First Alkaloids,” Historical Studies in the Physical Sciences 11 (1981): 321–22.

(36.) John. E. Lesch, Science and Medicine in France: The Emergence of Experimental Physiology, 1790–1855 (Cambridge, MA: Harvard University Press, 1984), 137.

(38.) William A Hammond and S. Weir Mitchell, “On the Physical and Chemical Characterization of Corroval and Vao, Two Recently Discovered Varieties of Woorara, and on a New Alkaloid Constituting Their Active Principle,” Proceedings of the Academy of Natural Sciences of Philadelphia (1860): 4-9, 8.

(39.) Mitchell, Researches on the Venom of the Rattlesnake, 95; and Matteu Orfila, A General System of Toxicology, or, a Treatise on Poisons, Found in the Mineral, Vegetable, and Animal Kingdoms, Considered in Their Relations with Physiology, Pathology, and Medical Jurisprudence (Philadelphia, PA: M. Carey & Sons, 1817), 10. For Orfila’s work, see José Ramón Bertomeu-Sánchez and Agustí Nieto-Galan, eds., Chemistry, Medicine, and Crime: Mateu J.B. Orfila (1787–1853) and His Times (Sagamore Beach, MA: Science History Publications, 2006). We have seen that Mead’s work also suggested a link between snake venom and exhalations. In Mead’s case, however, the goal was to offer a general account of poisons, whereas Mitchell no longer pursued this goal.

(40.) See, e.g., François Magendie, Lectures on the Blood and on the Changes Which It Undergoes during Disease (Philadelphia, PA: Haswell, Barrington, and Haswell, 1939); and Gabriel Andral, Pathological Haematology: An Essay on the Blood in Disease (Philadelphia: Lea and Blanchard, 1844): 17, 36–37.

(41.) Marcello Pera, The Ambiguous Frog: The Galvani–Volta Controversy on Animal Electricity (Princeton, NJ: Princeton University Press, 1992)Trumpler, “Verification and Variation.”

(43.) Ibid., 42.

(p.256) (44.) Ibid., 35.

(45.) Ibid., 45.

(46.) Ibid., 78.

(47.) Ibid., 47.

(48.) Ibid., emphasis added.

(49.) John Herschel, A Preliminary Discourse of the Study of Natural Philosophy (London: Longman, 1830), 151.

(50.) Auguste Comte, The Positive Philosophy of Auguste Comte (New York: Calvin Blanchard, 1855).

(51.) John Stuart Mill, A System of Logic vol. VII, Collected Works (Indianapolis, Indiana: Liberty Fund, 2006), 394.

(53.) Ibid., 311.

(54.) Kenneth Schaffner, “Clinical Trials: The Validation of Theory and Therapy,” in Physics, Philosophy, and Psychoanalysis: Essays in Honor of Adolf Grünbaum, ed. R. S. Cohen and Larry Laudan (Boston: Reidel, 1983). (p.257)

(55.) Bernard insisted that “experimental counterproof must not be mistaken for comparative experimentation. Counterproof has not the slightest reference to sources of error that may be met in observing facts; it assumes that they are all avoided and is concerned only with experimental reasoning; it has in view only judging whether the relation established between a phenomenon and its immediate cause is correct and rational”; Bernard, An Introduction to the Study of Experimental Medicine, 126–27.

(57.) Claude Bernard, Leçons sur les effets des substances toxiques et médicamenteuses (Paris: J. B. Bailliere et fils, 1857), 312–25.

(58.) This is one reason why Bernard never accepted statistics in physiology. I will come back to this issue hereafter. See also Porter, The Rise of Statistical Thinking, 160–62.

(59.) Ronald A. Fisher, The Design of Experiments (Edinburgh: Oliver and Boyd, 1935), 49.

(61.) He noted, for instance: “Almost all toxicologists who have investigated this subject, have been content to submit animals, as dogs, etc. to be bitten by the serpents themselves. We have seen, however, that when this course is followed, a number of fallacies interfere to prevent the observer from drawing satisfactory conclusions. …” He had tried to avoid these “embarrassments” by extracting and injecting venom; see Mitchell, On the Treatment of Rattlesnake Bites, 6, 11.

(62.) See especially Rosser Matthews, Quantification and the Quest for Medical Certainty (Princeton, NJ: Princeton University Press, 1995); and William Coleman, “Experimental Physiology and Statistical Inference: The Therapeutic Trial in Nineteenth-Century Germany,” in The Probabilistic Revolution: Ideas in the Sciences, ed. Lorenz Krüger, Lorraine Daston, and Michael Heidelberger (Cambridge, MA: MIT Press, 1987), 201–28. For more general treatments of statistics in nineteenth-century science and medicine, see Porter, The Rise of Statistical Thinking, 1820–1900; and Hacking, The Taming of Chance.

(64.) Pierre Charles Alexandre Louis, Researches on the Effects of Bloodletting in Some Inflammatory Diseases, and on the Influence of Tartarized Antimony and Vesication in Pneumonitis (Boston: Hilliard, Gray, and Company, 1836), 60.

(66.) Ibid., 137. Bernard referred to a controversy between François Magendie (p.258) and François Achille Longet about their experiments on the stimulation of the anterior root of the spinal nerve—a controversy that he had resolved. See Mirko Grmek, “Bernard, Claude,” in Dictionary of Scientific Biography, ed. C. Gillespie (New York: Scribner, 1970–1980), 30.

(71.) Ibid., 9.

(72.) I am not aware of Mitchell’s having had any financial interest in the production of antidotes.

(73.) Alan G. Gross, Joseph E. Harmon, and Michael Reidy, Communicating Science: The Scientific Article from the 17th Century to the Present (Oxford: Oxford University Press, 2002), 143–44.

(75.) Ibid., 45.

(77.) This is the chief difference between Mitchell’s report and the early modern presentation of experimental projects such as Redi’s, which also began with a particular question—the question of whether the yellow liquor was poisonous.

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