Whoever Could Get Rid of the Context of Discovery/Context of Justification Dichotomy? A Proposal Based on Recent Developments in Clinical Research

Abstract

In his Art and Illusion, art historian Ernst Gombrich argues that the emergence and development of styles of pictorial representation depend on the availability of certain schemata, which can be documented. He himself documents the schemata responsible for the emergence and development of several styles. Nothing of this kind has been done as far as the growth of scientific knowledge is concerned. In this article we discuss whether is it possible to document something analogous to Gombrich's schemata that can be of crucial relevance for the development of clinical research.

Keywords:

• discovery context
• justification dichotomy
• developments in clinical research

The question posed as this article's title brings another one with it: Is the context of discovery/context of justification dichotomy something that we should get rid of? Both Kuhn and Feyerabend are notorious for providing an affirmative answer. They were engaged in documenting the permeability of the scientific undertaking to social-historical contingencies and in establishing a philosophy of science that could take such permeability into consideration. They were perfectly aware of the vulnerability of a philosophy of science of such nature to the aforementioned dichotomy, and they could not do it without taking issue with it. According to them, this dichotomy should be put aside because it compels us to relegate to the “discovery context” certain peculiarities of the scientists' behavior whose importance for the advancement of scientific knowledge is absolutely crucial. When, however, it comes to pointing at some such unequivocally decisive peculiarity, Kuhn and Feyerabend take very different paths.

Kuhn points at the scientists' loyalty to a given tradition. Without the latter, Kuhn tells us, it is possible to have schools of thought, but no proper science. In the first chapter of The Structure of Scientific Revolutions he made it clear by mentioning that the discipline of Physical Optics existing prior to Newton fell short of being a science:

Anyone examining a survey of Physical Optics before Newton may well conclude that, though the field's practitioners were scientists, the net result of their activity was something less than science. Being able to take no common body of belief for granted, each writer on Physical Optics felt forced to build his field anew from its foundations. In doing so, his choice of supporting observation and experiment was relatively free, for there was no standard set of methods or of phenomena that every optical writer felt forced to employ and explain. (Kuhn, 1962, p. 12)

In clear contrast to Kuhn's perspective, Feyerabend's perspective is that the philosophy of science cannot relegate to the “discovery context” a whole set of Machiavellian practices such as adapting evidence to capricious ideas, turning to ad hoc procedures to dismiss or eliminate difficulties, or using ad hominem arguments that are essential to the scientific activity. It does not matter that in the eyes of some guardian of scientific rationality such practices may sound like the “most unscrupulous opportunism,” for without them there would be no science as we currently know it. Machiavelli pointed out that, in the actions of men against whom there is no court of appeal, the ends are what matters. Perhaps the essence of Feyerabend's “anarchic epistemology” rests in transposing this maxim to philosophy of science. After all, he would say, what could be wrong in systematically violating each rationally prescribed methodological canon, if the history of science shows that such violation often led the scientific venture to auspicious results? If history itself recommends procedures those epistemologists condemn—well then, too bad for the latter.

Admitting that both Kuhn and Feyerabend are right in their considerations on the importance of, respectively, loyalty towards a tradition and the “unscrupulous opportunism” (Feyerabend, 1988, pp. 72); peculiar of scientists' behavior, and that the differences existing between them may be somehow reconciled, would the aforementioned arguments then constitute a good reason for dissolving the discovery context/justification context dichotomy?

Let us begin with Kuhn. He wanted to demonstrate that, apart from considerations of a socio-psychological nature, nothing could be said about the scientific quality of Optics prior to Newton. He anchored himself exclusively into a consideration of a socio-psychological order—namely, that scholars dealing in Optics were not obliged to share any given body of common beliefs—to conclude that the “net result” of the activities conducted by those scholars was “something less than science.” Nevertheless, it remains to be answered whether the so-called “net result,” even while being “something less than science,” had any relevance for the development of Physics later on. We do not know whether the answer Kuhn has to offer is an aprioristic “no” or, simply, silence. But silence would be too big of a concession to the dichotomy which one wishes to get rid of. The aprioristic “no,” on the other hand, would imply the definitive encloistering of the aforementioned Optics in the 17th century. That is, it would preclude beforehand any attempt at verifying whether bodies of knowledge in past times do have any relevance to bodies of knowledge produced at some later time, be such later time a less remote past, or the present, or even the future. Actually, Kuhn's perspective inescapably implies such confinement. Already in the initial pages of The Structure of Scientific Revolution, he praises Alexandre Koyré's historiography of science for its zeal for the “historical integrity” of the sciences which are the focus of his studies. This historiography, he says, presents science from the perspective of its own time, rather than “seeking the permanent contributions of an older science to our present vantage” (Kuhn, 1962, p. 12). Instead of, for instance, investigating the relation existing between Galileo's concepts and those of modern science, it investigates the relation between Galileo's concepts and those shared by his group, that is, his teachers, contemporaries and immediate successors in science (Kuhn, 1962, pp. 4, 12, 119). Well, why then—we would object—can't we ask for the relation between Galileo's concepts and those of modern science? Why should we encloister Galileo's thoughts, beforehand, in the 17th century? We are afraid that Kuhn has no other answer to offer than saying that such questions only make sense within the framework of a historiography of science anchored on the concept of “development-by-accumulation.” Since it is, itself, tributary of the “discovery context/justification context dichotomy,” and since I consider such dichotomy as non-relevant, then I cannot engage in trying to answer these questions.

To Kuhn, as it all seems to indicate, the only means to reject the view—indeed, mistaken—according to which science advances by means of accumulated discoveries and definitively established truths is by preserving the “historical integrity” of the science of past times.

There is, however, another philosopher of science who, though (similarly to Kuhn) presenting himself as a fierce adversary of the discovery context/justification context dichotomy, is not in the least engaged in preserving the “historical integrity” of the science of past times. We thereby mean nobody other than Paul Feyerabend. In fact, in the abstract opening Chapter IV of his Against the Method, he lets us know that “any old, absurd idea is capable of improving our knowledge. Science absorbs the entire history of thought and uses it for the refinement of each theory” (Feyerabend, 1988, pp. 73). If this is so, and if the discussion focuses on the pertinence of the discovery context/justification context dichotomy, then the issue here is finding out how science “absorbs the history of thought.” Could it be that the Machiavellian practices so brilliantly described by Feyerabend have some important role to play in this process? So that the dichotomy may be dismissed, the answer must be an unequivocal “yes.” But would this be Feyerabend's answer?

To get to know what Feyerabend's answer would be, it suffices to read his enlightened reply to an objection raised by Mary Hesse against his thesis that “science absorbs the entire history of thought.” This thesis, argued Hesse, implies that even the most bizarre metaphysical system of the past may have left its mark in modern science. If this is true, then it should be worthwhile submitting such systems to criticism. It should be worthwhile, for instance, submitting to a critical review the modern science that would be present in Aristotelianism, or even in, say, voodoo. Given that a criticism of such bodies of knowledge is inconceivable—Hesse goes on to say—then it is senseless to suppose that there is something from such corpuses incorporated to modern science. Feyerabend's reply, we dare say, shows the extent to which his thought remained a tributary both of Popperian thought as to the dichotomy being discussed, despite his Herculean effort to get rid of both. In summary, his argument simply consists of showing that criticism against bodies of knowledge produced in the past is far from being a sterile exercise as Hesse supposes. Feyerabend writes:

Very often progress has been made thanks to a “critical review of the past,” exactly of the kind rejected by Hesse. After Aristotle and Ptolemy, the idea that Earth moves—an odd, old and “entirely ridiculous” Pythagorean concept—was dumped onto a pile of historical debris, only to be revived by Copernicus (. . .) Magic writings played an important role in this revival, still not fully understood, and were studied by no other than Newton himself. These developments are not surprising. One can never study all the branching of any one idea, and there is no concept which has ever been given all the attention it deserved. Theories are replaced by new versions which are more in accordance with the inclinations of their time, and are abandoned long before they have had the chance to display all their virtues. Furthermore, “primitive” myths and ancient doctrines only appear as bizarre and devoid of sense because their scientific content is either not known or has been adulterated by philologists and anthropologists who are not familiar with even the simplest physical, medical or astronomic knowledge. Voodoo, Dr. Hesse's pièce de resistance, is a case in focus. Nobody knows it and yet everybody refers to it as a paradigm for backwardness and confusion. Nevertheless, voodoo relies on solid—though not yet sufficiently understood—material basis, and a study of its manifestations could enrich us and perhaps lead us to review our knowledge of physiology. (Feyerabend, 1988, p. 73)

This effort to prevent old bodies of knowledge from being thrown away, without further consideration, onto a pile of historical debris—without which, incidentally, no history of science is deserving of this name—consists, in our opinion, of Feyerabend's greatest merit. But what lies underneath this endeavor? We think it is nothing else but our old dichotomy, which Feyerabend wants so tenaciously to get rid of. To test our point, let us examine it more closely. Why, according to Feyerabend, should voodoo be studied? Because it relies on “solid material basis, still not fully understood,” he replies. We are not sure what exactly some “solid material basis” might be, but, whatever it is, it is clearly something treatable apart from any socio-psychological approach—presupposing, this way, the pertinence of the discovery context/justification context dichotomy. Why could voodoo “lead us to review our knowledge of physiology”? Feyerabend does not answer this question, but his answer will certainly have to do with the assumption—we can't tell whether correct or mistaken—that voodoo, as a body of knowledge, contains propositions which somehow defy or complement, from a logical viewpoint, some of the propositions of our physiological knowledge. Again, whatever can occur within the scope of the discovery context is disdained. And what to say about the statement that

. . . “primitive” myths and ancient doctrines only appear as bizarre and devoid of sense because their scientific content is either not known or has been adulterated by philologists and anthropologists who are not familiar with even the simplest physical, medical or astronomic knowledge. (Feyerabend, 1988, p. 73, emphasis added).

or, still, about the assertion—so visibly subject to being directly attributed to Popper—that “‘one can never study all the branching of any one idea, and there is no concept which has ever been given all the attention it deserved?’” (Feyerabend, 1988, p. 73). What sort of light could Feyerabend's argument about the Machiavellian opportunism inherent to scientific practice throw over the reasoning presented in his finely drawn reply to Hesse? The discovery context/justification context dichotomy requires that the answer to this question be a laconic “no light.” We're afraid the answer is exactly this. How, then, to avoid the dichotomy, if it is at the basis of the commendable effort made by one of its fiercest adversaries to prevent bodies of knowledge produced in the past from being freely dumped onto piles of historical debris?

As compared to Feyerabend, Kuhn managed to keep away from our dichotomy in a more consistent way. In this case, however, coherence does not seem to be an advantage. There are medications whose continuous use may bring some discomfort, but if they are definitively abandoned the effects can be even more damaging. In such cases, it is not advantageous to keep consistently away from the medication. The same, we're afraid, goes for the discovery context/justification context dichotomy. We may perhaps do without it for a while, but soon the moment will come in which the associated damaging effects will make themselves felt. One such effect, as we have already seen, is that of being led to confining, as if by decree, any and every already-discredited body of knowledge to the pile of historical debris. Another and even more damaging effect (about which we shall speak further ahead) is that of making scientific progress an untreatable theme. For failing to remain coherent, Feyerabend managed to escape both effects. For being more coherent than Feyerabend, Kuhn could not escape from the first of these two effects. Fortunately, however, he was not coherent enough to the point of having to shut up about the nature of scientific progress. We will return to that point in due time. By now, we will focus the discussion on whether any gain could derive from Kuhn's relative success in keeping away from the aforementioned dichotomy.

In order to advance this discussion, we'll refer to the most Kuhnian book we have ever had the opportunity to read. The book in question came out prior to the advent of Kuhn, and in its preface we read: “‘I would feel proud should Prof. Popper's influence be felt everywhere in this book’” (Gombrich, 2000, pp. 23–24). We are talking about the magnificent Art and Illusion, by E. H. Gombrich, published for the first time in 1959. For the purposes of this discussion, it is sufficient to mention that Gombrich was striving to understand the process through which styles of pictorial representation take shape and evolve. One might look at, for example, a picture by Villard de Honnecourt, dated 1235 (Figure 1). The lion portrayed in it would certainly seem ridiculous to us. Today, even a reasonably talented child would be able to represent a lion with more verisimilitude. Admitting that Villard de Honnecourt was indeed a talented artist, and really intended to represent a real lion, why then a pictorial representation so scarcely truthful to what we suppose to be an “actual” lion? Would this have anything to do with a lack of real lions that could be more carefully observed, or with lack of a more precise knowledge of what in fact a lion looks like? No, replies Gombrich; this has to do with the absence of formulas or models from which to paint lions. These formulas are called schemata. In the 13th century, the repertoire of schemata available for a pictorial representation of lions would have been very poor, hence such an unconvincing “lion.” The same way as there are schemata for lions, there can be schemata for virtually anything: hands, feet, happy or sad eyes, cloudy and sunny days. Without a reasonable repertoire of schemata, an artist could do little. Where do these schemata come from? Often from previous works of art. A given painting represents, for the first time, a lightning bolt ripping through the skies. This “bolt” provides the material based on which various other bolt schemata are produced, some of which will be used by other artists in future. But, what about those situations in which art's function is not to provide verisimilitude? What to say of impressionist paintings, for instance? The same thing, Gombrich replies. The only difference is that, now, the schemata basically consist of paint blots. If Gombrich could, in his time, travel to the future and read The Structure of Scientific Revolution, he might say that, in the absence of a basic repertoire of schemata, on which artists could rely for their work, and to which they felt obliged to resort, then the “net result” from that which they might happen to produce would be “something less than art.”

FIGURE 1 Villard de Honnecourt: Lion et Porcupine. C. 1235. Pen and ink. (From Gombrich, E. H. [2000]. Art and Illusion. Princeton, NJ: Princeton University Press; pp. 176–177.)

There is, however, an important difference between Kuhn and Gombrich. For Gombrich can document how art depends on schemata in a way that Kuhn cannot duplicate when trying to demonstrate how science depends on conceptual schemes (Gombrich, 2000, pp. 23–24) provided by professional scientific training. Curiously enough, as far as this point is concerned, Gombrich is in a position to be more Kuhnian than Kuhn himself. Let us consider, for example, the beautiful painting by John Constable (1776–1837), “Cloud Study,” dated 1822 (Figure 2). Gombrich shows that this work could not have been produced without the previous existence of schemata of clouds, only available starting in 1785 in a book of drawings by Alexander Cozens, a landscape painter of the 18th century. Constable had access to the book, and copied a few of its schemata (Figures 3 to 6), designed to teach art students a variety of typical skies: “shredded clouds high in the sky” (Figure 4); “shredded clouds very low in the skies” (Figure 5); “half clouds, half fields, clouds darker than the field or dispersed by wind, and darker in the upper than in the lower areas” (6)—and so on, with all sorts of combinations and interchanges. Gombrich writes:

We know today what Constable learned from Cozens. It was not, indeed, the appearance of clouds, but a series of possibilities, or schemata, which deepened his awareness of them by means of visual classification (. . .) little does it matter which classification system we adopt. But without some standards of comparison, we cannot apprehend reality. Having seen Constable's creations, we can also see the clouds in a new way. (Gombrich, 2000, pp. 23–24)

FIGURE 2 Constable: Cloud Study. 5 Sept. 1822. (From Gombrich, E. H. [2000]. Art and Illusion. Princeton, NJ: Princeton University Press; pp. 176–177.)

FIGURE 3 Cozens: Sky template 1785. (From Gombrich, E. H. [2000]. Art and Illusion. Princeton, NJ: Princeton University Press; pp. 176–177.)

FIGURE 4 Constable: Drawing according to Cozens. (From Gombrich, E. H. [2000]. Art and Illusion. Princeton, NJ: Princeton University Press; pp. 176–177.)

FIGURE 5 Constable: Drawing according to Cozens. (From Gombrich, E. H. [2000]. Art and Illusion. Princeton, NJ: Princeton University Press; pp. 176–177.)

FIGURE 6 Constable: Drawing according to Cozens. (From Gombrich, E. H. [2000]. Art and Illusion. Princeton, NJ: Princeton University Press; pp. 176–177.)

Could there be anything more Kuhnian than this?

Kuhn himself, however, could not in his turn be so Kuhnian, as it was not possible for him to go so far in the demonstration—indispensable, by the way, if the aim is to dissolve the discovery context/justification context dichotomy—of how something so clearly subjected to being relegated to the realm of history or of socio-psychology of some product of human activity, be that product either science, art, or any other, can be so unequivocally responsible for the essential features of that product. In other words, Kuhn could not demonstrate that conceptual schemes and operational models learned by scientists in their professional training will account for the essential features of scientific knowledge the same way as Gombrich could demonstrate that schemata available in unpretentious drawing books would account for the essential features of different styles of pictorial representation.

To further clarify this point, we now return to Villard de Honnecourt's “lion” (Figure 1). We saw above that, in order to explain why this “lion” is so unlike a “lion” of our days, it is necessary to document existing schemata of a lion, or of parts of a lion, which were not available to someone who, like Villard de Honnecourt, lived in the 13th century. In a section of The Structure of Scientific Revolution, Kuhn seems to do something similar. The section we have in mind contains his discussion about Aristotle, Galileo, and swinging stones. From remote Antiquity, Kuhn tells us, many people had seen one or another heavy object swinging to and fro while hanging from a rope or chain, until reaching a resting state. To the Aristotelians, the swinging body was just falling down with difficulty, as a function of its being tied to the rope, until it got to a resting position which, according to them, was the state naturally sought by any given body. To Galileo, who had broken away from the idea that repose would be a more “natural” state than movement, the object in question was a pendulum, a body that just narrowly failed to indefinitely repeat the same movement. According to Kuhn, such transition took place because Galileo did not receive a totally Aristotelian education; on the contrary, he was trained to analyze movement in terms of the theory of impetus, a paradigm of the late Middle Ages, which had in Nicolau Oresme, a 14th century scholastic, one of its most prominent theoreticians. In Kuhn's view, Oresme outlined an analysis of the swinging stone that “‘is clearly very close to the one with which Galileo first approached the pendulum’” (Kuhn, 1962, p. 12). Assuming that all this is true, then what is Kuhn telling us? On the one hand, that there is logical compatibility between the propositions that constitute the theory of impetus and those comprising Galileo's pendulum approach; on the other hand, that Galileo resorted to the theory of impetus in formulating his pendulum approach. The first statement refers to the justification context; the second, to the discovery context. The dichotomy is thus kept intact. So as to dissolve that dichotomy in such a case, the theory of impetus would have to enjoy, in Kuhn's analysis, an analogous status as that of schemata such as those seen in Figures 3 to 6. Within the framework of such an analogy, the idea of a “swinging body falling with difficulty” would correspond to Villard de Honnecourt's “lion,” the idea of a “pendulum” would correspond to a more truthful “lion,” or, if so preferred, to a “lion” of any other style, while the theory of impetus would be the element responsible for that transition. But the theory of impetus, as any other theory for that matter, enjoys a degree of integrity and autonomy which is not seen in the schemata. Theories have a life of their own—as, by the way, Feyerabend so splendidly demonstrated in his Popperian retort to Hesse. They may be tested, have their ramifications investigated, be matched against other theories, evolve by confrontation etc., whereas all that there remains to be done in regard to poor schemata—whose fragmentary character, it should be added, is in radical contrast with the wholesome character of a theory—is to use them for a predetermined purpose. The schemata, thus, defy the discovery context/justification context dichotomy in a way that nothing described by Kuhn in his book does. The fact that it is possible to show its decisive importance for the emergence of a given style of pictorial representation apart from any consideration for possible social-historical contingencies under which the schemata may have been conceived enables it to escape from being relegated to the discovery context. On the other hand, the fact that schemata do not make up a wholesome body of knowledge (with its own life and propositions that may be related both to one another and to propositions originating from other bodies of knowledge) prevents their insertion into the “justification context.”

Having established that, it now remains for us to find out whether the fact that Kuhn has not gone so far in his attempt to bring into his philosophy of science that which the discovery context/justification context dichotomy declares as only being treatable in socio-psychological terms, namely, the very process through which theories are produced, is due to a correctable deficiency of his philosophy of science, or it is so because, having dealt with science, rather than with art, he really could not have gone any farther. Would there be any (documentable) thing so decisive for the production of a given scientific achievement (or, better said, for the determination of the essential features of a given scientific achievement) as the schemata represented in Figures 3 to 6 were in determining Constable's style? Perhaps there is. Table 1 presents the so-called CONSORT (Consolidated Standards of Reporting Trials) statement as a tentative answer to this question. Responsible for a very important and recent transition in the way clinical research came to be conducted, the CONSORT statement attempts to standardize the way a certain type of clinical research study is conducted, namely the randomized trial.

TABLE 1 Excerpt from CONSORT Statement

Heading	Subheading	Descriptor
Title		Identify the study as a randomized trial
Abstract		Use a structured format
Introduction		State prospectively defined hypothesis, clinical objectives, and planned subgroup or covariate analyses
Methods	Protocol	Describe
		Planned study population, together with inclusion or exclusion criteria
		Planned interventions and their timing
		Primary and secondary outcome measure(s) and the minimum important difference(s), and indicate how the target sample size was projected
		Rationale and methods for statistical analyses, detailing main comparative analyses and whether they were completed on an intention-to-treat basis
		Prospectively defined stopping rules (if warranted)
	Assignment	Describe
		Unit of randomization (for example, individual, cluster, geographic)
		Method used to generate the allocation schedule
		Method of allocation concealment and timing of assignment
		Method to separate the generator from the executor of assignment
	Masking (blinding)	Describe
		Mechanism (for example, capsules, tablets)
		Similarity of treatment characteristics (for example, appearance, taste)
		Allocation schedule control (location of code during trial and when broken)
		Evidence for successful blinding among participants, person doing intervention, outcome assessors, and data analysts
Results	Participant flow and follow up	Provide a trial profile [ . . . ] summarizing participant flow, numbers and timing of randomization assignment, interventions, and measurements for each randomized group
	Analysis	State estimated effect of intervention on primary and secondary outcome measures, including a point estimate and measure of precision (confidence interval)
		State results in absolute numbers when feasible (for example, 10/20, not 50%)
		Present summary data and appropriate descriptive and interferential statistics in sufficient detail to permit alternative analyses and replication
		Describe prognostic variables by treatment group and any attempt to adjust for them
		Describe protocol deviations from the study as planned, together with the reasons
	Discussion	State specific interpretations of study findings, including sources of bias and imprecision (internal validity) and discussion of external validity, including appropriate quantitative measures when possible
		State general interpretation of the data in light of the totality of the available evidence
Source: Moher, D., Schulz, K. F., & Altman, D. G. (2001). ‘The CONSORT statement: Revised recommendations for improving the quality of reports of parallel group randomized trials,’ BMC Medical Research Methodology, 1(2).

Randomized trials are a type of design used to compare the efficacy of different interventions such as drugs, treatments, or educational methods. Simply stated, the goal of a randomized trial is to learn which intervention works better. As its name states, randomized trials call for a random allocation of interventions whenever these interventions are to be compared. The random allocation of the intervention makes the groups being compared comparable in other ways that would influence their response to each of the interventions. For instance, suppose researchers want to test the quality of a new medication. They might select some patients with a condition that might potentially benefit from the medication and compare their progress with that of patients who receive a placebo—a pill without an effect. But the patients chosen to receive the new medication might differ from those who receive the placebo in a way that influences their final outcome—they might, for instance, be younger or have less co-existing diseases. Randomly allocating patients to the new medication or placebo decreases the possibility that the two groups will differ in a systematic way and thus compromise or bias the results. Randomized trials are therefore a method of generating defensible evidence about the relative efficacy of various interventions. For instance, in the 1954 poliomyelitis vaccine trials (Francis, Korns, et al., 1955, pp. 1–63), a trial design was used in an attempt to measure the efficacy of the vaccine's effect on the incidence of polio. Of importance, their results at the time demonstrated that the vaccine's effect was appreciably greater than estimates from a pre-existing series of non-randomized trials. In the context of our article, the 1954 poliomyelitis vaccine trials will be presented as an analogy to the lion of Honnecourt, where despite the acceptability of its research design in 1954, today this design would be promptly refused. This immediate refusal, we will argue, results from the influence of current scientific schemata that were not present at the time of the 1954 poliomyelitis vaccine trials. These schemata are represented by a set of accepted standards on how to conduct the comparison between interventions using a randomized trial. Examples of such standards include, for example, the random allocation of all patients in a random manner, a very specific description of how random numbers were generated, and a detailed description of how random numbers were hidden from participants and researchers to avoid bias.

The 1954 poliomyelitis vaccine trials were primarily conducted by the National Foundation for Infantile Paralysis (NFIP), using a combination of “placebo control study” and “observed control study” designs. The placebo control study was defined as:

Since the problem was to measure the degree of effectiveness, if any, of an untried product, it was important to have data which could provide an adequate gauge of the effect, free of possible bias in diagnosis and reporting. There was introduced, therefore, a [. . .] plan corresponding in pattern to that usually employed in scientific investigations. Children of the first, second, and third grades would be combined. One half would receive vaccine; the other matching half, serving as strict controls, would receive a solution of similar appearance which should have no influence on immunity to poliomyelitis. Each child would receive the same lot of material, labeled only by code, for all three inoculations. Only the Evaluation Center would have the key. [. . .] a number of well populated states indicated their preference for it and the “Placebo Control” study was incorporated into the field trial. It comprised 84 areas of 11 states with population in the first, second, and third grades of 749,236. (Francis et al., 1955, p. 1)

The above quotation was part of what clinical researchers and epidemiologists consider a standard randomized controlled trial and would not be criticized in its methods even by the most reputable medical journals. The other portion of 1954 poliomyelitis vaccine trials, constituted by the “observed control study,” had a different design described as follows:

The plan of procedure announced by the National Foundation for Infantile Paralysis and its Advisory Committee was to administer vaccine to children in the second grade of school; the corresponding first and third graders would not be inoculated but would be kept under observation for the occurrence of poliomyelitis in comparison with the inoculated second graders. [. . .]. The plan poses difficulties to objectivity in that knowledge of the vaccination status of a patient is readily determinable and the introduction of even unintentional bias can result; its adequacy would depend upon a high incidence and severity of disease, a high degree of effectiveness of vaccine, and the care with which the data were collected. A number of states, however, had already made their decision to participate on this basis. When finally arranged the procedure was followed in 127 areas of 33 states with total population in the first, second, and third grades of 1,080,680. (Francis et al., 1955, p. 63, emphasis added)

Although the authors state that this design would lead to “difficulties to objectivity,” the fact that this biased design was even pursued would be unacceptable for our contemporary scientific standards in clinical and epidemiological research. The excuse that “a number of states, however, had already made their decision to participate on this basis” would be considered risible, especially since, from the current perspective of our researchers, 1,080,680 children had been enrolled in a study considered completely flawed in its design. We are not claiming here that this flaw went unnoticed—the very disclaimer of “difficulties to objectivity” make it clear that even the study designers were aware of its problems, as were other researchers during that time (Brownlee, 1955, pp. 1005–1013). Our claim is that, for our current scientific standards, the “observed control study” would not even be proposed, not to mention the huge costs associated with unnecessarily enrolling 1,080,680 children into it. The question posed is, then, why would such a study design be acceptable by that time while today it would not even be considered? Our proposed answer is that, in analogy with the lion of Honnecourt, our contemporary researchers have templates or schemata used to discern between the right and wrong ways of doing certain types of research, exemplified by the CONSORT statement, which automatically allows them to identify research design patterns that deviate from the accepted standard.

The choice of analysis of the “observed control study” in the 1954 poliomyelitis vaccine trials was not accidental, since the refusal of this design by our current researchers is based on an easily identifiable schemata. In analogy to the book by Cozens where schemata for certain styles of pictorial representations were defined, in clinical and epidemiologic research the CONSORT statement (Altman, 1996, pp. 570–571; Begg, Cho, et al. 1996, pp. 637–639) has set the schemata that defines how a trial should ideally be reported. This schemata is clearly described in the almost dogmatic terms describing the CONSORT statement:

Randomized controlled trials are the best way to compare the effectiveness of different interventions. Only randomized trials allow valid inferences of cause and effect. Only randomized trials have the potential directly to affect patient care—occasionally as single trials but more often as the body of evidence from several trials, whether or not combined formally by meta-analysis. It is thus entirely reasonable to require higher standards for papers reporting randomized trials than those describing other types of study. (Altman, 1996, pp. 570–571)

The CONSORT statement schemata thus points to an ideal form, setting the stage for a multitude of evaluations about what is or is not adequate (Bath, Owen, et al., 1998, pp. 2203–2210; Adetugbo & Williams, 2000, pp. 381–385). As another example, the CONSORT statement not only claims that randomized trials are the “best way to compare the effectiveness of different interventions,” but it also tells researchers which aspects they should evaluate in a trial to check whether it is well-conducted. In other words, CONSORT tells what a randomized trial should “look like,” in the same way that Cozen's schemata told artists what clouds should “look like.” But how is this new in comparison to previous randomized trials, such as the 1954 poliomyelitis vaccine trials? Let us take the example of the random allocation of the placebo versus vaccine. Despite being an extensively documented trial with over 120 pages, nowhere in the document do researchers describe how the actual randomization was performed. For example, did they flip a coin to determine the sequence of random numbers, or did they use the “random number tables” that were widely available at the time? From the perspective of contemporary researchers, this is an absolutely crucial aspect since, they will argue, randomization is at the core of the study design and, if not appropriately performed, study results will be compromised. But why was this lack of information about randomization not even noticed by previous researchers while now this detail is so closely scrutinized? The answer, we will argue, are the schemata provided by the CONSORT statement. For example, one entire section of the CONSORT statement is exclusively dedicated to the description of details about randomization, clearly delineating the “unit of randomization (for example, individual, cluster, geographic),” the “method used to generate the allocation schedule,” the “method of allocation concealment and timing of assignment,” and the “method to separate the generator from the executor of assignment.”

If the parallel we suggest between the CONSORT statement and Cozzen's “clouds” is valid, then Kuhn has a point in his attempt to blur the discovery context/justification context dichotomy. However, we must say that even within the Kuhnian framework, the rejection of said dichotomy could not go unpunished for too long. In the final chapters of his book, Kuhn advocates that rejection not only because he understands that the referred dichotomy renders unfeasible any suitable understanding of the process through which science actually progresses but, above all, because he understands that the dichotomy masks the fact that “scientific progress,” now between quotation marks, is just the result of a peculiar way of telling the history of science. But, is it at all possible to speak of scientific progress, with or without quotation marks, without irretrievably committing oneself to the discovery context/justification context dichotomy? We are afraid the answer is no. Asking if and how science progresses involves, foremost, asking whether and why a given theory represents any gain in knowledge with regards to a previous theory, and such a question can only pertain to the justification context. That question separates the latter context from the discovery context in the same way a centrifuge device separates a liquid from the sediments contained in it. The only way to dissolve the dichotomy in focus is, therefore, by evading such a question, while keeping silent about the progress of science. Fortunately, neither Feyerabend nor Kuhn chose to evade the issue—as, luckily, neither could be coherent to the point of allowing the rejection of that dichotomy to guide them to that evasion. Both reserved a crucial role in their thoughts to the question put forth above. In the case of Feyerabend, this becomes clear when he strives, as we have seen, to show the importance of bodies of knowledge produced in the past for bodies of knowledge produced at a later time. As for Kuhn, it becomes clear when he strives to explain the importance of still-non-articulated theories for the progress of science. Insofar as Kuhn and Feyerabend got involved in such reflections of a clearly epistemological nature, and as, had they not done it, they would have seen their respective arguments on the social-historical character of the scientific undertaking reduced to a mere chronicle of science, both proved to be deep tributaries to the dichotomy which they so tenaciously sought to dissolve.