SCIENTIFIC FACTS AND SCIENTIFIC THEORIES

The Social Construction of Scientific Fact

In earlier discussion, it has been observed that observation and thought at the growing edge of science are obscure and difficult to assess, quite in contrast to all forms of epistemological outlook, which rely on hard data, on the idea that nature’s properties can conveniently be read in observation or experiment.

A clear and well-argued version of this approach is to be found in Part II of Ravetz’s Scientific Knowledge and Its Social Problems.² Ra- vetz’s book presents the first coherent account of how scientific activ­ity, which in its local form is always subjective and fallible, results in objective scientific fact as a result of a two-stage social legitimation process. The fleeting objects of laboratory perception, the tenuous marks of the data, become intellectual constructs with associated sci­entific objectivity as a social consequence of testing and (possibly) intellectual transformation. In chapter 3 of Part II Ravetz makes the very important point that scientific research is craftsman’s work. The individual experimental scientist is not a machine, noting pointer readings, counting blips, but rather he or she brings highly developed craft skills to the relevant tasks. Data, and hence scientific informa­tion, are dependent on the sensitivity of the investigator, his or her feel for the right workings of the apparatus, the correct choice of the right tools and techniques for investigating a problem, and so forth.

Ravetz also argues that reasoning in science, particularly at the growth points in science, is craft reasoning, a subtle blend of inductive, prob­abilistic, deductive, and analogical reasoning. This must be so at growth points because the interaction of data and theory is indeterminate. One does not know if the data are robust (i.e., roughly constant under slight perturbations of the experimental conditions), what the relevant data are, exactly, and what is evidence for what. Science assumes the familiar routine as these issues get settled, so that routine work can be made accessible to normal scientists—what Ravetz calls the “com­petence of mediocrity.” On this view, superior scientists have pos­sessed this aesthetic feel for their craft, and the unique social struc­ture of science enables these tentative and difficult original lines of reasoning to become hardened into determinate research strategies accessible to development by normal scientists.

In chapter 5, Ravetz argues that the craft nature of science pre­cludes a uniform methodology that suggests that scientific reasoning can be done in a semicomputerized fashion. It is possible that the view that scientific reasoning could be semicomputerized arises from taking physics (or mathematics or both) as the paradigm of science, another assumption binding the positivists, Popper, Kuhn, Lakatos, and even, to some extent, Ravetz himself. Physics tends to develop discourse about populations of physics objects that are theoretically equivalent. For example, physicists may talk about electrons, pho­tons, or whatever, classes that are very large and whose members are theoretically homogeneous with respect to their properties. Thus if a (random) sample of electrons or photons is obtained, and various properties are determined for this sample, it is methodologically straightforward to generalize about the entire population. Since sam­ples that are theoretically equivalent can be produced in many labo­ratories, this allows a division of labor in which “normal” science can easily contribute to the entire enterprise of physics.

Chapter 6 of Ravetz’s book introduces the social processes that con­vert the fallible individual research report (or rather, collections of such reports) into scientific knowledge. This process has essentially two stages. The first stage is the journal referee system, which con­trols the possibility of publishing research reports, and the second stage is the practice of citing earlier work in a field when writing individual research reports. Ravetz reports this as a descriptive soci­ological observation. He doesn’t argue that this system is the best way to enforce quality, and he doesn’t pretend that citable and valuable work can’t be lost in the workings of this system. It is simply that this has been the method of creating and authenticating scientific facts throughout the period during which science has been advancing at a suitable rate, and therefore it seems to Ravetz a fortiori to have been working pretty well.

Ravetz’s scientific realism makes facts, the basis of science, intel­lectual constructs that have survived this two-part legitimation proc­ess. The gap between this and any observationally foundational phil­osophical view is enormous. In Ravetz’s view, it doesn’t matter whether individual observations are theory laden or not; they are not the foun­dation of science. This is also why the teaching of science doesn’t proceed inductively from “foundations” in individual experiments, and why scientists are not much disturbed by philosophical attacks on the foundations of some branch of their subject. The hard data of science are at the level of legitimated fact, not at the level of philosophical epistemology. Or to put this another way, what is a fact for the indi­vidual scientist (e.g., preliminary data and a hunch) is not (at least not yet) a scientific fact. It should be obvious that the scientific facts in this view are something like superfacts, that is, after having gone through the two stages of legitimation they are, in some intuitive sense, more likely to reveal reality, or to describe features of the world, than are the deviant observations of individual scientists. Ra­vetz’s realism thus suggests an interesting foundational view for sci­ence of a kind that has not been explored in philosophical epistemol­ogy-

A practical problem is that it can be shown that important work may not be noticed and that minor work may be thought important, so that the sense of this judgment “more likely to reveal reality” re­quires discussion. Science is dominated at times and in places by “schools” of thought that are later seen to have been working in a direction that gradually gave out. Thus the realism here seems to contain seeds of relativism. But the historical examples show that while there are outstanding examples of good scientific work whose accept­ance into the scientific canon was delayed by bias, we obviously don’t have examples of truths that were never accepted into the scientific canon. There are many scientists, of course, who feel that their work isn’t being accepted fast enough, but motivation in science has re­mained high, suggesting that the working scientist normally sees the legitimation process as an acceptable hindrance or delay, rather than as a barrier to truth. Work of citable quality will be, in the common view, published somewhere, and then the author will have a chance to win recognition for it. It should also be noted that the publication of journals in science (and in academia generally) encourages debate. Without being “impartial,” editors will knowingly publish controversy and exchange in at least some small quantity—a factor that tends not to be so obvious in some religious, art, and political journals. All in all, then, Ravetz has made a good case that as a practical instrument traditional scientific legitimation has functioned conservatively on the whole, but superbly.

There remains the philosophical skeptic. It is logically possible on the basis of Ravetz’s realism that some important fact might be no­ticed by some individual who is incapable of communicating it to other scientists because of their conceptual blindness. But can this individ­ual be certain that he or she is right, that he or she possesses knowl­edge where others have merely opinion? The longing for methodology continues to reassert itself. Seen against the background of old movies in which a hero scientist is trying unsuccessfully to prevent a loath­some epidemic among ignorant villagers by some, to their minds, devilish scientific instrument, this may seem plausible. It is perhaps less plausible but still possible where a scientist is trying to convince other scientists about the worth of selected data. The plausibility it has here is considerably diminished by the problem of knowledge at growth points that Ravetz emphasizes. My single observation that the sun is shining, or that some other state of affairs obtains, may be knowledge in an established context where the language used to de­scribe matters is fairly settled and there is wide agreement about correct observation. But at growth points the evidence is typically so contradictory and complicated that those working in an area are well aware of the existence of problems and pitfalls and know that they need to strengthen partial views by more experimentation and by argument against other partial views.

We shall now examine the stages of the legitimation process some­what more carefully, beginning with the dubiety existing at the level of experimentation. For this purpose, a detailed case study by Holton will be employed.³ The point of this case study for our purposes will be the enormous complexity of craft manipulation required to get reliable results, and the sheer repetition of results until their stability was assured. Philosophers and sociologists have frequently simply overlooked the amount of effort required to produce the sort of classic experimental result grounding a scientific fact. Holton’s case study concerns a dispute that occurred between the physicists Ehrenhaft and Millikan about the value of the smallest electric charge, the neg­ative charge of a single electron. This dispute began in 1910, and its importance is related to the way in which the value of the negative charge of the electron is related to the calculation of other fundamen­tal physical constants. Millikan and Ehrenhaft were engaged in similar lines of experimentation, but Millikan found a stable smallest value for the electron, while Ehrenhaft found subelectron values, negative charges of a half, a hundredth, and even smaller fractions of the elec­tron’s charge. This dispute lasted for over twenty years, although with historical hindsight it is easy to see that Millikan was right and Eh­renhaft wrong. At least it is easy to see this provided that modern postulated subelectronic charges do not become a reality, although even in this case it seems relatively obvious that these charges should not have played a role in Ehrenhaft’s experiments. The dispute is made more interesting by the fact that Millikan observed subelec­tronic charges from time to time, but dismissed them as artifacts caused by experimental error. From the contemporary viewpoint, Ehrenhaft was also the more distinguished physicist. Of further interest is the fact that the general emergence of the stability of Millikan’s experi­ments permitted scientists to “see” individual electrons, a fact cutting against the view of phenomenological physics, which held that atoms and smaller particles receive ontological significance only as organiz­ing principles for direct observations in experimental settings. In short, this dispute has the attributes of emerging significance that have been argued for in our historical discussion.

Millikan began his research with the conviction that there was a unit charge, and that the experimental means for determining it were fairly obvious. Before Millikan’s work, those proceeding on a similar assumption had only been able to calculate the average charge on a population of electrons. Millikan began along the same track, with the idea of simply making small changes in existing procedures in order to improve accuracy. Water droplets were produced in an expansion cloud chamber in the standard procedure, some then falling at the gravitational rate, but others (charged) falling more rapidly in an elec­tric field imposed on the droplets. A number of simplifying assump­tions were required to interpret this experiment, such as the assump­tion that the droplets were similar or that ionization did not substantially affect the size of the droplets. Millikan and a collaborator began by ionizing a moist gas prior to cloud formation in a new way, and in so doing they substantially improved previous results. This newer value was of help to Rutherford in another connection. In discussing Milli­kan’s work, Rutherford suggested that it could be further improved, and pointed out in particular that evaporation in the experiment was probably underestimated, causing the calculated value of the charge to be too small.

To study the effect of evaporation, Millikan used a much stronger battery to create an electric field that could hold the singly charged layer of droplets steady against the influence of the gravitational field. The result of this stronger field was to destroy the observable cloud, including the layer of presumably singly charged particles. What hap­pened, as it turned out, was that the droplets were actually variously charged, and the field caused them instantly to separate, hence the disappearance of the cloud. With this exposure of a false supposition, a decade (note the time period) of cloud watching as a means to ob­serving the value of the charge of the electron came to an end. Then Millikan noticed that although the cloud was dispersed, some few droplets remained in place, stationary in this strong field, presumably just the droplets that were singly charged. Attention now shifted to watching singly charged droplets held stationary in an electric field, instead of a falling cloud of droplets. Millikan also noticed that some droplets, apparently catching a new charge, would suddenly begin to move decisively. Observing these suddenly moving droplets, Millikan calculated that charges seemed to come in integral multiples of the basic charge, confirming the conviction of unit charge.

Millikan’s first major paper on the new method was presented in 1910, and included a critique of other methods of measuring the unit charge, including Ehrenhaft’s. In his paper, Millikan divides his ob­servations into those that were “best,” those that were “good,” those that were “fair,” and those that he discarded. The craft nature of observation is manifest. Millikan relied on his feel for the correct working of his apparatus, and was also constrained by his anticipation that good observations should cluster around the correct value. Better observations were therefore weighed more heavily by Millikan in working up the data to produce a calculated mean value for the unit charge. Ehrenhaft, reacting to Millikan’s critique, began a series of new experiments utilizing a quite different technique from Millikan’s in which he reported fractional values of the electron charge. Further, he subjected Millikan’s paper to a countercritique, showing that a differing mathematical workup of Millikan’s data actually supported the doctrine that there were subelectronic charges. Clearly, where Millikan saw divergencies in his data as clustering around an assumed correct value, Ehrenhaft saw Millikan’s data, like his own, as a dis­persion of values, indicating fractional charges.

At various times, Millikan tried droplets other than water droplets, but the breakthrough to his famous experimental determination of the unit charge of the electron came when he tried utilizing oil droplets rather than water droplets. This minimized the uncertainty of various theoretical assumptions, such as the assumption that evaporation was not affecting the experiment, and the stability of oil droplets allowed Millikan to boast that he could observe a fixed number of charges on such a droplet as long as he liked. The previous dispersion of values literally disappeared, and the number of observations that had to be considered poor, or discarded, dropped enormously. In the mean­time, equipment components were improved, a better optical and timepiece, as well as better temperature, pressure, and electric field control. Although improvements were made for years, the first run of oil drop experiments dramatically reduced the probable error in the calculated mean of the unit charge, and forecast the eventual resolu­tion of the controversy over its existence. After five years of pursuing some form of droplet experiment, Millikan was now ready for a long series of runs on the oil drop experiment to clinch the view that it established the unit charge beyond question. In one six-month period (note the time interval) from October 1911 to April 1912, Millikan ran 140 experiments in which individual oil droplets were observed as they picked up charges. A paper published in 1913 on this series (and on other series) that singled out 58 drops as the data base for a mean value produced a value that Millikan accepted for twelve years, de­spite constantly improving technique. Many of the drops studied were not included in the data base because of suspected equipment or ob­servational failure. These judgments were not included in the 1913 paper, as they had been in the paper of 1910. Millikan’s self-doubts were obviously a thing of the past. The better technique allowed him to more sharply distinguish good results from bad results, and his confidence also measurably increased as it became clear that the unit charge could be more successfully integrated into the body of physical theory than Ehrenhaft’s fractional charges, leaving as the only open question its precise determination.

This episode will stand here for many that might be taken from the history of science. An early line of experimentation is almost acciden­tally selected as promising, and then refined in a series of trials and errors, as well as by the consequences of at least two sharp insights, the method of using a strong enough field to hold the drop steady and the switch from water to oil droplets. There is a convergence from vague perception to a reliable technique, and then a sustained series of concentrated observations clinching a basic value, at least in the theoretical context of the times. The constant craft nature of the scheme is shown in the fact that Millikan’s experience gradually produced clear data (“beautiful,” as it is described in his notebooks) although the equipment cannot produce clear data for the uninitiated, for ex­ample, contemporary beginning students of physics. Controversy with Ehrenhaft and the constructive criticism of Rutherford gradually set the direction in which experiment took place. Original dubiety about the calculated value, coupled with exposure of a wide range of data, gradually became transformed into near certainty about the value, coupled with exposure only of the data relevant to that calculation. In time, this method of calculating the unit charge produces the value that is quoted in other work as a fact on the basis of which other calculations can proceed. These are the features typical of the devel­opment of a fixed experimental datum that our abstract discussion has led us to expect.

We can now turn to the conversion of subjective judgment into objective fact over the life of citation of some proposed finding. The initial filter discussed by Ravetz is the process of refereeing before publication. Success in this process is recognition of the fact that in the opinion of one or more peers, work is of more than minimum quality, making it a possible object of scientific controversy and scru­tiny. What this process lacks in objectivity is shown informally by the fact that a paper may be rejected by one journal and then accepted by another journal. Within disciplines and research areas, an informal ranking of the quality of journals may cause a tendency for articles to be submitted to journals of decreasing perceived quality, so that final acceptance is a partial measure of the strength of what would be con­sensus about the paper’s quality, but this has been little studied. We are interested here in the change of modality that occurs when work becomes more widely cited, and the author or authors discover that recognition for their work is increasing. Fleck had noticed in 1935 that journal articles may contain modalities such as “I have tried to prove... or “It appears possible that... ” or “It cannot be conclu­sively established...” that are consonant with the stage of contro­versy over the significance of contents.⁴ As significance becomes set­tled in science, and the resultant facts become fixed points in review articles and later work (and ultimately in textbooks), the modalities are stripped away until only assertion remains. Fleck, studying the relationship of the Wassermann reaction to the concept of syphilis as a disease, noted that the correlation of positive Wassermann test re­sults to confirmed cases of the disease rose as the reagents and timing of the test were manipulated until the test could generally be seen as reliable.⁵ The literature involved in the serodiagnosis of syphilis by means of modifying and simplifying the Wassermann test reached, on Fleck’s estimate, ten thousand journal articles.⁶ In this case, the de­velopment of technique and the phase of controversy before consen­sus about fact are enormously complicated.

This point can be developed in greater detail using an example from an analysis of scientific work in biomedical research at the Salk Insti­tute by Latour and Woolgar.⁷ After a discussion of how controversy shifts the status of scientific statements between various layers of a typology ranging from mere conjecture to assertion of fact, Latour and Woolgar offer an analysis of the construction of one scientific fact: the discovery of the structure of a peptide whose function in the endocri­nology of certain mammals is the release of thyrotrophin. The poten­tial value of this fact lies in its role in helping to explain how the human brain may control human behavior by utilizing such releasing factors. This discovery was made principally as the result of research undertaken in two rival laboratories between 1962 and 1969. From 1969 to 1971, this discovery was frequently cited by other researchers in their papers. A marked decline in citation from 1971 to 1975 oc­curred as the suggested structure became a fact that could be taken for granted, and by 1975 textbooks reported this structure as a fact that had been established by the two laboratories in question. Ra- vetz’s account of citation requires some refinement to allow for this pattern of increasing and then decreasing citation followed by text­book representation, which may well be a general pattern for scien­tific literature, especially successful literature.

Biomedical research in the relevant area consists of attempting to match the action of natural substances to that of synthetic counter­parts. A natural substance may have a known effect on an animal, or on the cells, muscles, or whatever, of such a creature. This substance can be split into subcomponents and the effect of the subcomponents on the animal, cell, muscle, or whatever compared to that of the original substance. In this way, which is methodologically crude in its logical structure but tremendously sophisticated in its instrumental realization, researchers attempt to isolate and purify the entity in the natural substance responsible for the effect of interest. The purified entity can be analyzed partly through the use of various techniques, but the exact structure of the entity cannot, in general, be determined by analysis. To find the exact structure, researchers attempt to syn­thesize the entity from pure amino acids (and other building blocks) by techniques that allow them to understand what they have synthe­sized. This process of synthesis is guided by the clues provided from analysis. When a substance is synthesized that matches the effect of the purified entity from the natural substance, the structure of this purified entity is then thought to be understood. This process can be nearly dialectical when analysis restricts synthetic possibilities, whose exploration can restrict analytic possibilities, and so on. Further, after identification, slightly divergent synthetic forms can be explored for their potential in therapeutic medicine.

From 1962 to 1966, most of the work on the substance of Latour and Woolgar s example was based on the expectation that it was a peptide. Early research showed that the action of the substance was destroyed partially or totally by certain enzymes and by heating with hydrochloric acid. These crude tests for peptidic nature resulted in the following language:

In this note we show arguments in favour of the peptidic nature of these substances....⁸

As the language shows, this evidence was not conclusive. In the next few years, further work, which failed to show an increase in the ratio of amino acids as the extract was purified and failed to destroy the effect of the substance with more sophisticated enzyme tests, led to the tentative conclusion by one of the laboratories that the substance was not a peptide:

We have been led to question the long held hypothesis that [the substance in question is] of peptidic nature.⁹

The other laboratory, now entering the field, also confirmed the new hypothesis that the substance was largely nonpeptidic, but it was puz­zled by its own discovery of the presence of amino acids in a per­centage suggesting peptidic nature:

The results are consistent with a hypothesis that [the substance] is not a simple polypeptide as has been thought previously, but nevertheless our evidence indicated that 3 amino acids are pres­ent in this molecule.¹⁰

In reaching this conclusion, the second laboratory was clearly influ­enced by the work that had been done in the first laboratory. By 1968, a number of new techniques imported from other fields and a massive amount of brain extract led to new results and a realization that the problem was enormously complex:

Our efforts at characterizing the chemical structure of [this sub­stance] have led us to the conclusion that we are dealing with a rather difficult problem for which classical methodology is turn­ing out to be of only limited significance.¹¹

In other words, the particular nature of the substance precluded the use of normal techniques, such as the use of gas chromatography, for which the substance was not volatile enough. Special techniques needed to be developed. The new techniques came from chemistry, and they revealed that the rejection of the peptidic nature in 1966 had been a mistake. The breakthrough came from the synthetic direction. Possi­ble combinations of the amino acids found in the new analytic assays were tried and dramatically lessened the number of possibilities. Fi­nally, a better way of analyzing the purified natural substance was discovered, and the possibilities were reduced to one. The purified natural substance was no longer said to be similar to or like the syn­thetic compound: rather, it was said to be identical with the synthetic compound, and this fact then became a given in research and a com­monplace in textbooks. Both laboratories produced histories in which they were primarily responsible for the discovery, but they are now usually given joint credit.

This example shows quite clearly the shift in modalities as the rel­evant fact came into view, and it indicates that the significance of the research in 1966 was not apparent until better experimental tech­niques were available in 1969. A curious and not uncommon inversion in significance had taken place because of a changing background of accepted possibilities. Evidence toward a peptidic nature for the sub­stance first became available, then evidence pointing away from this conjecture, and finally evidence for a peptidic nature as the evidence was measured against an increasing array of theoretical possibilities and experimental techniques imported from other fields and adapted to the specific nature of the problems in this research area. Curiously, after the structure was discovered, an enzyme was discovered that might have set the research of 1966 on the right track. Therefore, the evidence takes on an even further shifting quality when it is set against possible scientific backgrounds, and its historicity is confirmed by the inclusion of such possible contingencies in its evaluation. The discus­sion and examples of this section should be sufficient to indicate why it is more revealing to consider scientific facts as constructions than as mere careful observations, and why this shift in descriptive termi­nology does not mean a concession to any easy relativism.

Data Domains

Biological species adapt to environmental niches, but adaptation may be a complex phenomenon. Species may fit into neighboring or new niches successfully when such an opportunity exists because the niches are open, or because they are filled with other species that can be driven out. Species may also alter the niches to which they are adapt­ing by changing them physically, or by altering the total ecological balance so that the relevant niche changes in terms of food possibili­ties or the nature of existing predators. Change need not occur solely on the side of the species. Environmental changes not attributable to the species, or attributable only partly to species activities, may pro­duce a change in the nature of the adapting species, if only in the distribution of variety within the adapting species. Because of this dialectical interplay of species and environment, it is possible to argue that any sharp distinction between species and environment is a con­ceptual illusion. Such illusions, however, may be necessary at least on a temporary basis for understanding. To some extent, the inter­action of species and environment is simplified by the perceptual ap­paratus of the species, which simplifies the total range of possible environmental changes into a smaller set of signals to variations in which the individual members of the species have the capacity to respond. This fact allows the internal workings of the members of the species to be studied against limited environmental changes. Such studies allow insight into the means by which individuals can respond to environmental change and the limits of such means. Although the­ory and fact are locked in dialectical interaction on our view, a similar conceptual framework can be used to freeze the data and study the response of theory to fixed and slightly varying data. Similarly to the biological case, there are good methodological grounds for fixing the data and studying the means by which theory can adapt, rather than the reverse. The relative simplicity of the organism or theory with respect to its environment allows one to project a comprehensible possible range of adaptive tactics against a relatively fixed environ­ment, whereas the total range of possible environmental change must remain largely unknown.

If the sensory apparatus of organisms simplifies environmental change and reduces it to a set of signals to which the organism can respond, it is clear that successful species will have sensory apparatus that is, in some sense, matched to those features of the environment that are most indicative of the biologically relevant aspects of its environmen­tal niche. Success will depend on the availability of a suitable range of responses to change, but it also depends heavily on a suitably dis­criminating sensory apparatus, one attuned to the most important en­vironmental indicators. Theories adapt to fact in similar ways, refining the facts so as to yield a conceptually clear version of their signifi­cance, and then projecting a range of possible facts attached to pos­sible new observational locations. At any given time, the set of pos­sible facts will be enormous, and a theory will typically reduce this set by discriminating between relevant facts or relevant features of facts, or both, and those facts or features it will ignore. Given what we have said about the significance of fact, some theories will take a losing gamble. They will adapt to facts or features of facts that do not stabilize as the environment is explored and perception becomes more refined and sensitive. In the long run, the projections of such theories will prove unreliable, or less reliable than those of theories that hap­pen to fasten on the facts that do stabilize and are significant in re­vealing environmental change. Our historical point that facts emerge from a social process in science reveals why Popperian falsifiability is such a misleading notion. To falsify a theory, the significance and stability of a fact must be given with its putative isolation. A specific fact may be lethal to a very specific theory making an extremely spe­cific prediction, when it is isolated, but the more usual case is that the isolation of a putative fact will not destroy a theory, which is best conceived as a bundle of specific interpretations of a set range of pos­sible facts, just as a species is a bundle of specific genotypes, but it will tend merely to change the distribution of its interpretations. The theory may constrict the niche in which it is viable, but to drive it to extinction will require a great many adverse facts whose permanent significance is regarded as settled, as well as perhaps suitable com­petition or predation.

The total possible set of environmental niches for species can’t be described. What we can do is match existing species to the niches in which they have proved viable and project possible niches in which they might also succeed. When this is done, it is clear that the avail­able niches usually have shifted over time, but also clear that some available niches are not filled until suitable organisms develop. If we wish to define data domains as factual niches to which theories adapt, by analogy to the environmental niches to which species adapt, we have to deal with the problems of defining environmental niches that are shifted to the new area of consideration. The problem of individ­uating niches has a number of serious aspects. The individuation of niches is constrained in nature by the biological possibilities because new organisms adapting to such niches must somehow result from the possible reproduction (allowing for mutations and meiotic scrambling) of existing forms of life. In the scientific case, discriminations of mu­tations from new forms becomes much more a matter of convention. In both cases, we have the problem of separating true niches, into which viable species can adapt, from false niches, where species will fail because their sensory apparatus and repertoire of responses are insufficient to continue life.

Man’s environmental niche was originally constrained by his sen­sory apparatus plus the discriminations in perception that could be coded into ordinary language. This niche has been considerably broadened by science. The instruments of science can best be seen as refining and extending human sensory apparatus, and scientific lan­guages as refining and extending the discriminations that can be coded into ordinary language. As a result of these extensions, more people can remain alive, and can remain alive under more varied circum­stances, than would be possible without science. Specialized theory, like any specialized conceptual apparatus, will permit relevant dis­criminations to be made and acted on in individual data domains, but the scope of theory will be related to the extent of such a domain. In technology and special skills such as cookie baking or horse breeding, an activity will be extended and refined. In science, it is our pure sensory apparatus that is extended and refined. Telescopes and mi­croscopes extend human vision, and not a particular activity, and they provide new objects that science can see, describe, and theorize about. The individuation of data domains thus stems ultimately from the hu­man sensory apparatus and its instrumental refinement and augmen­tation in science. Objects of ordinary perception become separable into objects of extraordinary perception, but extraordinary percep­tion, even when it seems to be dealing with an autonomous world, receives its significance from significance in ordinary perception. Modern sophisticated measurements of length, for example, have humble origins in such beginnings of instrumentation as are repre­sented in this sixteenth-century instruction:

To find the length of a measuring rod the right way and as it is common in the craft... Take 16 men, short men and tall ones as they leave church and let each of them put one shoe after the other and the length thus obtained shall be a just and common measuring rod to survey the land with.¹²

Because data domains must be individuated for the adaptation of the­ory, and because they are constructed through instruments whose most sophisticated operations are ultimately read by the human per­ceptual apparatus, some kernel of anthropomorphism remains in even the most advanced science, no matter how little subjectivity remains. Further, just as sight may yield vague, confusing, or ambiguous data, and sight and hearing (or any other pair of sensory modalities) may conflict, these extended data domains cannot be expected to be free of perceptual problems and the attendant process of eliminating those theoretical conjectures that misread the perceptual field.

The objectivity of certain features of the world is given in science as it is in ordinary perception by the repeatability and robustness of perception. That my house is on the east side of my street is sup­ported by its always being there whenever anyone looks. In the ex­tended and augmented perception of science, repeatability and ro­bustness cannot be taken for granted. Instruments must be developed that will allow repeated observations to be made and will locate the same features on repetition, at least for trained observers. Objective observation of fact is not in question until the level of fact described as a result of the social process of negotiation in the last section is reached, and until instruments are available that permit the fact in question to be ascertained by scientists with divergent interpretation of theory. Here we will stress the role of instrumentation in fixing the limits of data domains and in locating the facts within them.

People with different interpretations of situations may well see dif­ferently, and it has not proved philosophically fruitful to attempt to find a level of seeing at which everyone is said to see the same thing, so that differences are explained as differences of interpretation of this basic level.¹³ Now let us consider an everyday example. Two people who wish to move a desk through a doorway disagree about whether the desk will fit through the opening. The person who believes that the desk will not fit may see the desk as being larger than it appears to the person who believes it will fit through the opening. Our inter­pretations of situations, our beliefs about situations, and our theories about data may influence the perception of situations and data. In fact, since it will do so, the absolutely neutral observation of fact re­quired in many forms of empiricism and rationalism is an illusion and cannot be proven to exist. Empiricism and rationalism could not prove its existence, but depended on a transcendental argument that such observation was necessary to ground the objectivity of science. These arguments we have laid aside. It is interesting to notice what an in­strument accomplishes. An instrument breaks the line of influence from interpretation to observation, or from theory to fact. Both per­sons interested in moving the desk may locate a ruler of some kind, and then be in a position to agree that the measurement of the desk is sufficiently larger or smaller than the door opening to settle the question of whether the desk will fit without trial and error. The measurement may result in the discovery of the fact that the desk is narrower than the door, or vice versa. Incidentally, given the hazards of measuring, a sufficiently similar measurement for the desk and the door may not settle the argument, and even the settled argument may be mistaken because of some other fact, for instance, that the door can’t be opened widely enough to expose the whole doorway to the desk because of some feature of building design. The use of the ruler also doesn’t reveal a brute fact, but rather a shared interpretation or belief, since the ruler can establish the relevant facts only if it is agreed that the ruler is of the same length in both relevant locations, and so forth. Naturally, this agreement may be tacit, and not con­sciously arrived at. What we have here is a situation in which opposed viewpoints must yield to the fact that the desk is about twenty-eight inches wide (let us say), and the doorway thirty inches wide. The world is still interpreted, but the individual interpretations have been modified.

Scientific instruments function like the ruler in the example, at least when the significance of their use is widely accepted. Instru­ments function to break off the influence of assumption on personal observation. If they did not exist, the fact of the influence of theory on perception might mean that shared data would be impossible. Where they do exist, a level of objective scientific fact of the kind analyzed in the last section is more likely to be achieved. The instrument is usually a machine. Properly used, it stays the same from experiment to experiment, and its reduction of data complexity to a common sig­nal, like a number expressing a reading, tends to neutralize what may be a highly variable scientific temperament from experiment to ex­periment. In physics, where instruments are plentiful, domains of scientific fact are numerous and in many cases clearly individuated. In sociology, where instruments are not plentiful, theory tends to penetrate through to observation, so that two sociologists may see the same limited situation in quite divergent terms, and instrumental re­duction of the divergence may not be possible.

Another way of marking the influence of instruments on the objec­tivity of data, breaking the influence of theoretical expectation on ob­servation, is the following. As we have repeatedly observed, the data gathered at the growing edge of science are confused and uncertain. It is exactly in this area that theory can be seen to guide perception. Bacteria, investigated by the early microscopes, were at the limits of resolution, and could be seen as having almost any shape. Saturn and Mars, investigated by the early telescope, were of ambiguous config­uration, and could be interpreted by different investigators as having divergent features. The existence of new particles in elementary par­ticle physics can depend on whether a double peak in a graph is deeply enough separated on a histogram. At the limits of instrumen­tation at any given time, who can blame scientists for finding confir­mation of those views to which they have committed their research, even if this confirmation is muted in the research report?¹⁴ The im­provement of instrumentation can remove this ambiguity. Where ex­pectation had caused divergent perception, a common construing of the data may take its place.

The ruler in our desk-moving example can be used in connection with many different problems. Similarly, many general scientific in­struments—the telescope, microscope, spectrometer, voltmeter, chronometer—are used in a variety of scientific investigations, and they presumably work the same way in each of their applications. This helps to circumvent a problem about falsifiability that has been pro­posed by many authors. A theory will, in many cases, predict an ob­servation only in the context of auxiliary theories, at least some of which are involved with the instruments required to make the obser­vation. If an observation incompatible with the theory is made, it can be argued that the blame could be assigned either to the theory or to the auxiliary theories. But auxiliary theories involved with instrumen­tation may also occur elsewhere in science, and the scientist is not in a position to argue that they are false only in his or her area of re­search, provided that the instruments are working well elsewhere. This fact constrains falsification in the direction of the primary theory and away from the auxiliaries, and blunts considerably the mere log­ical point that the falsity of the conclusion to a valid line of reasoning may be the result of the falsity of any of the premises. That instru­ments are used by different scientists in the same research area and are also frequently used in different areas of research means that the facts they uncover, and that they produce such and such data in such and such circumstances, is not under the control of the individual scientist. No matter what facts are agreed on, the choice of a theoret­ical interpretation of those facts from available alternatives is a matter of personal decision. A scientist may choose to evaluate new instru­mental findings as artifacts of experimental design, and as not requir­ing theoretical interpretation, but this involves the gamble that these findings will not survive the legitimation process and become scien­tific facts. One can perhaps more gracefully change theoretical stance in the light of new facts than one can admit to having looked at solid findings and set them aside as errors.

The independence of theory from fact that instruments help to cre­ate is reflected in the history of instrumentation. Scientific purposes for which the instrument is to be used need not be involved in any detail in refinement and improvement of the instrument. Refining instruments is a craft process and is not necessarily led by theoretical reflection. Aside from the obvious fact that the light telescope was to magnify distant images, improvements in the smoothness of surfaces of lenses and mirrors and in the means of mounting and moving the telescope to ensure solidity could be carried out quite independently of the theoretical curvature of light to be interpreted by the instru­ment. To a certain extent, the working of the instrument can be ex­plained in ordinary language, and the working of the instrument is not dependent on the data augmentation and theoretical advances its use helps to bring about, along with the specialized languages re­quired to express new data and theory. The telescope augments hu­man visual perception. Without long-exposure photographic comple­mentarity, the telescope allows one to see what could be seen from a different and closer position with the naked eye, especially when the constant distortions and visual artifacts of the telescope system are filtered out through familiarity with its use. Different interpretations of the resulting observations are possible, but the resulting observa­tions cannot at first be influenced by full theoretical expectation. As is well known, the first observations of Saturn produced a variety of interpretations of its structure, a variety that was quickly narrowed down as a result of theoretical advance.¹⁵ The early interpretations occurred in an earlier language, and were not yet in the full grip of theory. What is seen as a new kind of data, such as the data first revealed by a new instrument, must be described graphically, as like what is already known. As theory develops, description can become much more detailed, but expressed in the descriptive terms of the new theory, with a resulting loss of vividness.¹⁶ As will become clear, instruments, data, theory, and language all tend to evolve into close consonance in many areas of science, but instruments play the essen­tial role of initially separating data from theory so that a direction of accommodation can be plotted.

If the importance of instruments as stressed here is correct, why do histories of science and books on the philosophy of science pay so little attention to the details of instrumentation? The indexes of such books typically include an overwhelming number of entries to people and to ideas, but not to specific instruments. Many books are written with titles like “The Conceptual Development of Quantum Mechan­ics,” or “The Conceptual Foundations of Quantum Mechanics,” but very few with titles like “The History of Instrumentation Used in Quantum Mechanics.” In most books of history or philosophy con­cerning science, experiments are described in only the most abstract terms, for example, “In this experiment, a beam of electrons was passed through a narrow slit and...” Some means of reconciling this fact with the importance of instrumentation stressed here is requisite.

Although instruments produce new data, some of which become legitimated scientific fact, we have already argued that the legitimated scientific fact is the foundation of scientific epistemology. Instru­ments, which in many cases are necessary to produce this level of fact, lie below this level once it is established. The data and legiti­mated fact guide the development of theory. Since there are points at which data become fact, these can be treated as fixed points for theoretical development. Of course, theory influences the develop­ment of instruments, but theory never becomes fully legitimated at quite so narrow a moment in time as fact. Instruments, like eye­glasses, are used to see things, but they need not be noticed (unless they malfunction or break) once what is seen through their use takes on independent existence. When the significance of a fact is known, the fact is important, but the details of its discovery no longer matter save as a source of possible heuristic advice for other scientists, or as part of the history of an area of science.

A more important omission of reference to the details of instrumen­tation may seem to be the relative lack of attention given this topic in journal articles. An instrument can be named or illustrated in an article, or a modification in technique noted. These sorts of references do occur. But the feel of an instrument and an explanation of its work­ing cannot easily be accomplished verbally. Theory and data can be described, but one must learn how to operate an instrument. In most research areas, a common set of instruments for investigation is a given of research strategy, and new instruments are generally bor­rowed from known research areas. An understanding of the workings of these instruments and their limitations is part of the common knowledge of research groups, a fact insufficiently noted in Kuhn’s discussion of paradigms and in other attempts to explain unity in sci­entific understanding. Any attempt to develop this for outsiders would run into the difficulties of explaining technique verbally, but there is no need to explain this to outsiders in journal articles, since they are not addressed to outsiders. Learning to understand instruments and their use is a staple of scientific education, and is accomplished ap­propriately in the laboratory practice of laboratory sessions run in conjunction with lectures on the relevant scientific topics.

In the view of history proposed here, instruments are important at the growing edge of science. Their primary significance is to contem­poraries. They define the kind of data it is possible to obtain, and the limits on that data. When the data have been legitimated, they drop out of consideration. This is probably why instruments have not been noticed by philosophers as a real constraint on data text, and it helps to explain why reference to instruments does not occur where one might initially anticipate it. Our understanding of scientific history, however, cannot overlook this feature.

Data domains cannot be defined in terms of instrumentation alone. Some instruments are used to define different domains, possibly in conjunction with differing sets of related instruments. We have em­phasized that new instruments can produce new data domains or be developed to explore new data domains, but we need to distinguish between the refinement of an old instrument and the development of a new instrument, no matter how blurred this line might be in prac­tice. We can’t have difference in domains distinguishing new instru­ments from refinements and also pretend that new instruments, rather than refinements, individuate new domains. We have been working with a basic analogy between theories and species, on the one hand, and data domains and environmental niches, on the other. The prob­lems with discussing the relationship of species to niche have already been mentioned. An alteration in a species may change the niche it adapts to, and the discovery of a niche by placement of a few mem­bers of a species in it, perhaps because of an accidental translocation and subsequent impossibility of returning to the old niche, may trans­form the old species, possibly into a new one. It is hard to regard either side of such an interesting pair of concepts as fixed. In the case of theory, because of the same sort of historical considerations, it will be adapted to, and adapting to, a data domain whose nature and ex­tent have some permanent features given by legitimated fact, and some newly discovered features given by a set of instruments re­garded as in interaction with the set of objects the theory is concerned to talk about. A variant of a theory can suggest a new or an enlarged niche for itself. At the same time, a new niche may be encountered by instrumentation, and representatives of older theories may enter such a niche, but then undergo such drastic change that they trans­form into new theories. But the temporal sequence may not be so crude, and the interaction of data domain and theory may be ex­tremely complex. As in the case of speciation, any change in theory (or in the distribution or nature of its subordinate interpretive var­iants) may cause a change in its related data domain, and vice versa. How extensive a change is required before we recognize a new do­main or a new theory is a matter of conceptual convenience that has little to do with subtle variations in the real process being described. Just as wild changes in developmental forms, or forms for different times and locations, can be seen as variants of a species, because the niche being adapted to in some sense requires these forms, so wild change in theory can best be seen in many cases as adaptive response to a changing data domain. Two variants can be seen as different versions of the same theory, variants of two conflicting theories or totally distinct in terms of the data domain to which they are directed. Logic must simply view them as distinct and lose the process of ad­aptation over time.

The problems can be illustrated with the light telescope. Theories of the nature of the universe existed before the telescope and were based on naked eye observation. An understanding of how heavenly bodies are related, how they move, and so on is a good example of interpretation of a domain given to all human experience. Before Gal­ileo’s use of the early light telescope, his predecessors had used a few instruments, but only to support and refine naked eye positional ob­servations of the heavenly bodies.¹⁷ Galileo’s use of the telescope clearly opened a new domain in which, for example, the phases of Venus and the existence of sunspots called for dramatically new kinds of theory. Galileo himself regarded the telescope as adding a new and superior sense to man’s panoply of natural and common sense. The telescope thus marks a sharp break in knowledge. Even if the Copernican turn could be argued for in terms of theory applied to the old measure­ments, telescopic observation of new kinds of objects relentlessly pro­duced totally new kinds of theories about heavenly objects. But new objects were discovered as the light telescope was refined and aug­mented with timed photography. Galaxies, star clusters, nebulae, and so forth, objects as new as the phases of Venus at the time of Galileo’s discovery, were discerned gradually as the telescope was improved. Theory changed in response to these discoveries, but the immediate problem is whether the refinement of the telescope produced new data domains, without the telescope becoming a new instrument. Be­cause the theory of the expanding universe, developed to deal with the discovery of galaxies and their observed motions, is quite incom­patible with most previous theory, it would seem compelling to see new data domains here, and that could be justified by the inclusion of new instruments and techniques that were required to measure the red shift, and so on. The point of introducing the notion of data do­mains is independent of the details of resolving such puzzles. Without the notion of data domains and the associated notion of how instru­ments are essential to their exploration and to defining their extent, the history of the interaction of theory and data becomes a series of arbitrary adjustments in which the constraints felt by contemporaries are totally absent.

Any full account of instrumentation would require a discussion of the fact that instruments are developed that are quite general in na­ture, such as the telescope, microscope, and spectrometer, that can be adapted to research in many different areas, and that for the quite specific purpose of demonstrating some important fact, such as At­wood’s machine for demonstrating Newton’s second law.¹⁸ These lat­ter instruments may have a complicated evolution with respect to the data they are designed to obtain. A more general instrument will be developed along common lines, small advantages and refinements oc­curring in a manner that can usually be anticipated, but a manner subject to the problems of craft improvement. In the development of the laser, as reported by Collins, there were many laboratories at­tempting construction of a more powerful gas laser by increasing the operating pressure of the device.¹⁹ The general usefulness of the de­vice was recognized, and attempts to increase pressure without ob­taining breakdown in operations were proceeding along uniform lines, with many laboratories constructing essentially the same design. Op­eration of the laser is uncertain, at best. Sometimes it will work sat­isfactorily, and other times not, without explanation, and a model built to the specifications of another will not perform in the same way. This is an interesting example of the problems of operating equip­ment, and Collins is interested to observe that competition between these groups resulted in less than ideal communication between them. What is interesting here is that communication was not perceived as needed in many cases because the general design was a given, and the various groups building such lasers were looking for variants that would result in better working through a trial-and-error or craft ap­proach. For many such general instruments, one would expect differ­ent instruments to be constructed on different sites, all of which might be regarded as variants of the same instrument.

The search for an instrument to demonstrate a specific fact can be quite different. Collins also reports on a variety of attempts to con­struct a device to observe gravity waves in order to confirm the gen­eral theory of relativity.²⁰ Here a race is on to discover gravity waves, predicted by a theory, in a manner that will make their existence a legitimated scientific fact. In this area, at the time when Collins wrote, one person had claimed to obtain data showing gravity waves, but this did not produce a rush toward design of a similar apparatus. The data of the first scientist had only been partially communicated, but it was clear to many of his competitors that his data might not, or would not, produce legitimated fact. They therefore explored different kinds of apparatus in an effort to find convincing and repeatable data. Even those who were tempted to accept the original finding were not anx­ious to be second. In all of these efforts, there was a conscious inten­tion not to produce the same apparatus in order to have an opportu­nity to receive recognition for first establishing this important fact. As we have seen in the case of Millikan and Ehrenhaft, two scientists expecting different data to be legitimated may quite consciously choose to investigate some given data domain with quite different instru­ments. These examples may be sufficient to establish that the history of instrumentation would be no passive narrative, and that the rela­tionships of the instruments developed to the data domains they ex­plore may be quite complex when viewed in detail.

The Microprocessing of Scientific Fact

Continuing the biological metaphor that has played an important role in this chapter, we may consider the case where the environment changes very little over a period of time, and the species filling a niche in this environment has sufficient genetic flexibility to adapt closely to its niche. Under these circumstances, the species and the environment will reach a close relationship of adaptation in which the species will attain a distribution of members that will remain stable over time. The sensory apparatus of the species will also show con­formity to the major features of the environment requiring response for appropriate homeostasis to exist, and a delicate balance of prop­erties on both sides can be achieved not unlike that between sym­biotic partners. In the scientific case, there is a gradual coincidence of the properties of theory, data, and instrumentation where appro­priate theoretic flexibility exists to match the texture of reality as re­vealed in the gradually legitimized data obtained from suitable instru­ments. This is hardly surprising, since it can be viewed as an extension of linguistic adaptation to prominent features of the surrounding world in ordinary life and language, although in this case the sharper split noticeable in science between theory and data is more difficult to discern. Of course this difference is precisely what is to be expected, since ordinary language vocabulary can be expected to have resulted from the settlement of many disputes and the accumulation of many observations about those features of the world of most importance to a wide class of human beings in the pursuit of their interests. In this section, we will consider in more detail this inherent drive toward coincidence of language and fact where only small perturbations of data and slight divergencies in theoretical outlook are in question. The full dialectic of accommodation of theory and fact will occupy us in the next section.

Our running engagement with some of the major philosophies of science receives an interesting update in this connection. What Kuhn regards as normal science and sees as the typical activity of the ma­jority of scientists is closely related to the phenomenon to be dis­cussed. In a great many areas of modern science at any given point in time, theory, data, and instrumentation will be in sufficient con­sonance that current work will be appropriately seen as an extension of previous work, fitting theory more closely to data, and data more closely to theory, with improved and refined instrumentation an im­portant desideratum in the process. In this context, a few anomalies can be seen as of little immediate importance. The paradigmatic back­ground is not necessarily a shared set of values so much as a shared data domain and style of language, the two having adapted sufficiently that fact and value, data and theory, have become inextricably woven in the activity of scientists. Science at a local level need not have progress as its goal, but achieving fit between language and fact. In medicine, for example, research programs may seek a test to define a disease and definitive treatment for the disease so defined. A fully successful small research program will degenerate and stagnate as it attains success, leaving a known cure as a residue. Investigators will then turn to other research problems. In physics, a similar phenom­enon is to be observed. The laws of the inclined plane are settled, and textbooks may refer to fixed solutions to what were once live research programs. The piling up of settled problems does not, as noted earlier, provide a general definition of progress, since the per­centage and significance of solved problems in a field require assess­ment, and there is the problem, waived as a presupposition here, that what is settled may become unsettled when new data, new instru­ments, or new theory attacks the convergence of language and data in some area of science. Kuhn’s account misses the impact of new instrumentation and new data, which can create a new data domain whose adapted theoretical form will typically be obtained by sudden crossbreeding from the existent stock of theoretical ideas.

Popper is wrong to see permanent revolution as the goal of science. The instrumentality of science to solve new problems may harden if new domains and theories for them are not developed, but settled domains are a necessary and desirable feature of scientific history. If new human relationships require new literary invention, it does not follow that definitive treatments of such staples of human interaction as anger, lust, and sorrow do not exist in older literature that we should want to keep. Similarly in science, where various practical problems remain common to our past, and for which appropriate sci­entific knowledge exists.

What individuates research programs and their theories is con­tained in the notion of data domains. For this reason, it is not nec­essary to postulate, as Lakatos does, a fixed hard core defining theo­retical identity. All of the researchers attempting to fit a given domain may evaluate the conscious theoretical formulations differently, one researcher seeing as central what another holds open to debate. This possibility seems more closely instanced in the actual divergent opin­ions of scientists than the notion of a paradigm or hard core suggests, but it requires a relational view of theory and domain. Further, re­search programs may progress or degenerate quite independently of their final significance in scientific inquiry. A research program solv­ing fewer and fewer problems may be approaching appropriate con­sonance of language and data in some important area, or it may be unable to adapt to relevant data produced by a new or refined instru­ment. Finally, a call for new theories and new research programs is somewhat quixotic in the absence of domains to be filled. A more desirable call is for preserving diversity of existent theoretical variants over known data for the purpose of maximizing the recombinant pos­sibilities of theoretical concepts known to be viable when data de­mands new theory.

The situation to be discussed in science can be seen most clearly in mathematics. We can regard the various number systems of mathe­matics as data domains to which theories have been adapted. For simplicity, such further domains as vector spaces, matrices, geometric planes, rings, and fields will be omitted from this discussion, but sim­ilar observations would be relevant. For example, for the positive integers the number of prime numbers, the number of twin primes, the truth of the Goldbach conjecture, and so forth have been matters of theoretical dispute, some of them settled. In contrast to science, the data domains of mathematics are perfectly precise, and they are not subject to significant perturbation after they have been clearly marked out. Further, many theoretical claims about such domains are either true or false, and no real dubiety about the matter exists after the construction of appropriate proof. As a result, the logic of falsifi­cation works quite neatly, and significance is frequently obvious (be­cause related only to truth or falsity in a domain) at the time when various proposals are put forward. Positivists and others have fre­quently treated science as though it were like mathematics, with pre­cise domains and facts within them, and with clear methods for de­termining truth or falsity. Positivism might have provided a satisfactory epistemology for science if science were like mathematics in terms of having clear data, the significance of which is resistant to change over time.

The instrument of mathematics is proof, and this instrument has been in use, although with refinements, at least since Pythagoras, Euclid, and the other Greek mathematicians in the relevant tradition leading to modern science. As in the scientific case, instrument and data domain can interact, as is shown brilliantly in Lakatos’s study of the interaction between proof and counterexample leading to a settled concept of polyhedron.²¹ In Euclid’s work, the extent of plane geom­etry and the domain of positive integers are not quite coincident with modern notions related to axiomatics and formal proof, but these data domains have shown a remarkable stability, and for the most part Euclidean proof is easily adapted to modem standards of rigor. There are no continuous data domains of this longevity in the scientific tra­dition. It is not surprising that mathematics and astronomy should have developed early in our view, since their pursuit, at least initially, was not dependent on sophisticated instrumentation.²² The excite­ment of mathematics for a philosopher like Plato must have been the first adumbration of the organic theoretical growth of scientific theory based on settled foundation in fact. Plato’s skepticism about empirical theoretical knowledge was appropriate until the rise of an instrumen­tation that could permit legitimated fact to arise.

In mathematics, data domains are constructed or invented by the human mind. Provided that methods of proof for extending these do­mains do not encounter inconsistency, there is nothing that could change them. Invented domains can have very complicated struc­tures, with various notions of proof exposing different structure within the domains. Domains may wax and wane in terms of their interest to mathematicians, and domains may be shown to have the same structure or some other logical relationship that is of significance for methods of proof and the typology of mathematics, but certain kinds of surprises can be ruled out. Imagine the discovery that a mistake has been made all along, and that there is no fourth positive integer. By contrast, the significance of fact in the data domains of empirical science is subject to revolutionary shift with the discovery of new data. Entities thought to be identical may diverge, and vice versa, and the discovery of new entities may completely change the refer­ence class of possibilities for what was already thought to be under­stood. Of course, even mathematical ideas and domains like the pos­itive integers need not be given full blown. As Klein and Bloor have noted, Greek conceptions of number, and our own, are somewhat divergent.²³ To obtain the structure of the positive integers as a fixed data domain, decisions must be made about the first integer (is it a divisor, and is it one of the positive numbers?) and about the infini­tude of the collection, and these decisions will interact with simplicity of proof and theorem, the acceptance of mathematical induction as a valid form of proof, and so on. Yet the structure of the positive inte­gers can be discerned in Euclid in much the modem form, and al­though extensions of this structure to the full number line occupied mathematicians for twenty centuries and more, theorems about the structure of the positive integers have remained intact throughout this period.²⁴ There is currently little research on the positive integers. Although not all problems about this structure have been solved (the Goldbach conjecture, Fermat’s last theorem), it exists in solid analogy to the settled domains of science discussed earlier. The permanence of data domains, once appropriately constituted in harmony with ac­cepted standards and styles of proof, seems the major touchstone for understanding the differences between mathematics and science that have intrigued a number of scholars. This permanence, related as it is to human invention, helps to underscore the importance of instru­mentation in enabling the continuous creation of new data text in the empirical sciences. Mathematics must deal with the data domains found intelligible and consistent by human beings. Their relative sim­plicity and frequent recurrent features, and the difficulty in inventing genuinely new and useful mathematical data domains, underscore the relative lack of complexity of inventions of the human mind in contrast to the constant frustration imposed on human theorizing over reality, the unanticipated richness of whose structure has subverted every known attempt at consistent conceptual description in other than lim­ited and partially abstracted domains.

Some theorists have drawn a sharp distinction between the arts (and also possibly law, theology, and the humanities) and science, and have then attempted to place mathematics in between, as sharing some features of both science and art.²⁵ When science and art show too many similarities, it is assumed that something must be wrong with the given methods of analysis, since the distinction between them is taken as an important phenomenological given. But it is simply possible to consider painting, for example, as a series of styles gov­erned by shared outlooks and attacking various technical problems in much the manner of scientists in history.²⁶ In this view, shifts in style may look like shifts in paradigms or research programs, and painting may exhibit a diffuse notion of progress not unlike that which we have been grappling with in science. In all of these areas, the successes of the past can be incorporated into the vocabulary and techniques of the present, so that it is possible to be a contemporary practitioner without detailed historical knowledge of one’s discipline. Nonethe­less, knowledge of the history of one’s discipline may be most useful to artists and humanists, less useful to mathematicians, and least use­ful to scientists. Are we then dealing with some sort of a continuum?

What seems to matter most is not the relevance of history, but the existence of data domains and theorizing about these domains. It is being suggested here that mathematics and science form a continuum in this dimension in which the range is specified by precision and permanence of data, coupled with the possibility of permanent exten­sion of data text. Between science and mathematics will be found abstract theorizing over ideal types, objects not found in the real world, such as perfect gases and frictionless surfaces, but objects sharing the dimensions of real world objects, with simplified properties and sub­ject to idealized instrumental investigation yielding precise data sim­ilar to that obtained in mathematics. Mathematics shares with science, and shares most closely with idealized science, accuracy of theoretical prediction and the possibility of refutation of prediction through the accumulation of data. By contrast, the arts and humanities deal with the description and interpretation of relatively fixed texts, and with problems capable of expression and resolution within the limits of ordinary language and experience. Ordinary language and experience may be stretched or extended in the arts, but it is not augmented into a language for specialists. This observation, of course, would re­quire modification for recent extensions of the humanities that have been influenced by the style of the sciences, and have searched for autonomous subject matter and autonomous languages and relevant evaluation only through expertise, but the origin of the sharp phe­nomenological distinction between science and art must lie in atti­tudes formed before these recent and quite problematical develop­ments. We can consider a few examples. Western painting has represented worlds of general human interest (albeit in a succession of styles) through similar technical means for centuries, and has only recently moved in many quarters away from traditional anthropo­morphic subject matter.²⁷ In this tradition, the human figure may be described and rendered from many points of view, all of which are consistent within the confines of relative description. There is no an­alogue to prediction and refutation, save where a theorist or painter contrives to predict the direction of painting or the public response to some style. In theology, the texts to be interpreted are notoriously set in advance through the appearance of God or prophet in human history. Although interpretation must be made contemporary to be credible, such general problems as the distribution of evil in God’s kingdom can remain problems of interpretation of the same text for centuries, and the notion of the instrumental augmentation of data achieves no purchase in this situation. Whatever the complexities in­volved in relating science and art, it seems likely that mathematics will always show close differential affinities to science, and will remain bound to science in such discussions through the existence of math­ematical scientific theories interpreting idealized data that character­ize postulated idealized objects. The differences between mathemat­ics and science are to be related to the consonance of theory and data more easily achieved in mathematics, and the permanence of that consonance as a result of the invented nature of the data domains. What has been noted as a difference in history is then primarily to be explained as follows: Some domains and theories achieve a perfect fit in mathematics, and then no longer change over time, no matter how useful the theories may be. Research interests then shift. Mathemat­ical systems, which develop an invented domain, can be terminated by inconsistency, or have their range restricted by impossibility proofs, but they are not so subject to counterexample by unexpected data. Unexpected data cause revision, but also lead to retention of what has been shown, quite in accord with the classical positivist view of sci­entific history. By contrast, domains in science are likely to be deeply reevaluated when later instrumental augmentation of data text pro­duces totally unanticipated consequences. Fewer settled theories of any longevity are to be expected in scientific history.

Kuhn, in a recent discussion, compares mathematics to art: While stagnating traditions die out in each, stagnating traditions may be pre­served for their utility in application in science.²⁸ In this connection he cites two interesting papers by Fisher on the death of a mathe­matical theory, specifically invariant theory.²⁹ Although Fisher dis­cusses what he sees as differences between some of the sciences and mathematics in his articles, this pairing by Kuhn is somewhat mis­leading. Perhaps no one paints seriously in certain past styles in the present. The number of invariant theorists is not quite so small.³⁰ Our textual comparison between science and mathematics results in the expectation that the distribution of mathematicians would change more dramatically than the distribution of scientists after consonance be­tween language and data, or after the appearance of counterexample. In Fisher’s view, the problems of invariant theory were to a large extent solved by a famous and unexpected proof by Hilbert, greatly reducing its scope, and it was reduced to nearly total stagnation as interests shifted to vector and tensor theory, as well as to axiomatics as a proof style, in the early decades of this century. The reason for sharp shifts in mathematics is the relative clarity of the logic of math­ematical proof and counterexample as a result of the precision of both theoretical consequence and data. Mathematics may mimic art in stagnation, but the mechanisms are different. Art interests shift with saturation of style and boredom with a technique, whereas mathe­matical interests shift when challenging problems are solved. Further, contrary to both Kuhn’s and Fisher’s impressions on this point, it seems that essentially solved domains are retained in both mathemat­ics and science, although they will be more numerous in mathemat­ics.³¹

After consonance of language and fact is achieved in science or mathematics through social legitimation, it may seem quite marvelous that language should fit reality so closely. The usual correspondence theories of truth trade on the established fit between ordinary lan­guage and the world, or between contrived calculus and idealized domain. In the case of ordinary language, a close fit in many areas was achieved long in the past and the amount of noticeable current change is small. Because of this achieved fit, it is rare that one cannot describe and evaluate, for ordinary purposes, whatever one confronts, at least as far as the limits of language are concerned. New words frequently seem to be only abbreviations for features of the world that can already be described with greater circumlocution in the linguistic resources already available. In mathematics and science, the process of achieving this consonance is more open to inspection, since new data domains and linguistic resources to describe the domains are always undergoing a forced and painful development. Once clear statements of fact have been achieved through instrumental investi­gation, the reference of fact seems fixed and objective, and indeed it is. The world has been discovered to show a fixed and repeatable response in certain interactions as described in the language, and this response is an objective consequence of these interactions. Even mathematics and scientific theorizing, like certain other forms of fic­tion, can be viewed as limiting cases of this generality, where the response to interaction is a highly idealized version of actual responses designed to preserve features of simplicity in the language used to describe that response. This process of achieving or constructing ref­erence for language by development of a domain we will call the microprocessing of fact, after discussion of this phenomenon by La­tour and Woolgar.³² When the process is complete, the evidence of microprocessing disappears, and mere correspondence, the very cor­respondence that has been slowly and carefully constructed, is all that remains.

We can start with a mathematical case, by considering the concepts of integer and set. The domain of integers has been investigated for more than twenty centuries, and was adumbrated earlier in the proc­ess of counting. What an integer is seems clear and straightforward, and whether or not something is an integer is open to a principled inspection in the relevant mathematical cases. There is an identifiable zero, and all the other integers can be reached from this zero by a simple operation. The relationships of positive integers, negative in­tegers, odd integers, even integers, prime numbers, and so on are so well understood that the domain has a clear outline, clear methods of proof, and only a few unsolved problems. Terms such as positive in­teger have clear reference, and code into their significance the reso­lution of disputes that were live in Greek times, but have been settled for centuries. For example, the term integer, in contrast to the term number, literally codes the generally recognized fact that the integers do not exhaust the numbers, and so on. There are integers. This much is beyond dispute even though there are various philosophical explications of the implied ontology. When we turn to sets, every­thing changes. The total domain of sets has been explored for less than a century, and disputes into its extent and nature remain unre­solved. Various axiomatic treatments of set theory, for example, differ in the language that they use, and even differ over whether certain sets belong to the appropriate domain of investigation. In comparison to the concept of an integer, the concept of a set seems fuzzy, except to some partisans of fixed approaches. The social process of negotia­tion here is still so obvious that some expert mathematicians believe that the paradoxes and problems of set theory will never be totally resolved, so that set theory remains a useful tactical instrument, but is not the appropriate theory for discussing foundations of mathemat­ics along the lines that have been pursued by set theorists in the first half of the twentieth century. The microprocessing of set theoretic facts has not been completed, and the reference of set theoretic lan­guage remains somewhat shifting and uncertain beyond various sim- pie consensual examples. Whether there is a clear domain of all sets and an appropriately sharp ontology referencing set theoretic lan­guage remains an open question.

Between mathematics and the experimental investigation of reality lies an area of mathematical theorizing in which empirical content can be simplified and greatly extended by taking on a mathematical form. Here we find idealized objects capable of mathematical description and mathematical development in theory. Typically, the empirical data will resist idealization, but a fit between mathematics and reality of sufficient closeness can sometimes be forcibly achieved that allows mathematical anticipation of reality, allows a way of anticipating pat­tern in data.³³ The planets do not behave exactly as in Newton’s cal­culations, nor do gases as in Boyle’s, but the mathematical theories of both anticipate fact that could not be gathered from mere accumula­tion of data. We have noted the descriptive fit between ordinary lan­guage and reality, but there is a predictive gap. The weather can be described, but not predicted reliably according to a theory expressed in ordinary language, as well as the fact that comets can be described, but not the timing of their appearances, and so forth. Predictive gaps can be filled in by constructing a mathematical model of reality and then predicting the nature of idealized events within the model. Slip­page between precise prediction and observed fact can then be used to fine tune the model, and so forth. There is no satisfactory philo­sophical explanation of the widespread success of this process in sci­ence, but its dialectical contribution to scientific advance is part of the epistemological description of scientific knowledge being urged in our study.³⁴ Some of the mystery is removed by seeing this dialectic as existing between pure mathematics and experimental inquiry. Pure mathematics deals with even more idealized data. Objects are, for example, to be merely counted, and mathematics can allow us to pre­dict the result of a total count by summing partial counts. Where this is successful, and we must learn through experience where it is suc­cessful, we can utilize mathematics to avoid the wholesale transloca­tion of objects in the world to obtain a full count, even though objects are hardly as neatly individualized in the real world as they are in mathematical representation. Exactly how the mind can match math­ematics and empirical fact remains a puzzle, but the matching is the secret of scientific epistemology and its dialectical progress. Discov­eries such as that of Neptune by Adams and Leverrier depend on the supposition that theoretical and empirical description can be brought into arbitrarily close coincidence through refined instrumentation coupled with sufficiently clever mathematical idealization.³⁵ Had Ad­ams and Leverrier maintained a Platonic separation of world of being from world of becoming, looking at a specific place for a specific ob­servation could not have confirmed or refuted any sound theoretical position. The role of instrumentation in bringing coincidence of the­oretical and observational language, and the ability of modern math­ematicians to construct idealized mathematical representations of real­ity for test through instrumental observation, are jointly responsible for the explosion of scientific knowledge since the seventeenth cen­tury.

The dialectical interplay of feet and theory in this vast middle ground of scientific theorizing depends on the existence of sufficient legiti­mated fact to give a domain stability, and to provide a language in which the domain can be described. As in the mathematical case, legitimation of fact involves modalities and obscure reference. Scien­tists are interested to know whether their statements refer to facts “out there,” or reference mere artifacts of experimental or theoretical technique.³⁶ During legitimation, investigators may be idealists, rel­ativists, skeptics, realists, and so forth, as the evidence shifts with respect to their scientific intuitions. Genuine epistemological debate will fuel the controversies required to develop the relevant data do­mains. The factual status of a substance will shift along with the mod­ifiers required in its description by evidence. A better language, as well as better instrumentation, will be a desideratum of investigation. When consensus is reached, it is not surprising that language and fact will mesh. Language will contain terms for the facts that have stabi­lized in the investigation, and the facts that have stabilized will call for a referencing term in the language used to describe the domain of which they are a part. Statement now matches reality because they are two aspects of the result of the same process of exploration and negotiation. It is only after statements match reality that they can be “about” it in the dialectic of science. And the fact and the language may melt once again into indeterminacy as the terrain of domains involved in science shifts. A term like gene was once obscure, then clear, and then obscure again, as biology developed. A term like ether was once clear, then obscure, and then clear again, as cosmology de­veloped. As we move to empirical science, the possibility of cycles of significance arises in a manner not anticipated in everyday life or mathematics, where terms usually only acquire significance and then retain it, although terms may become obsolete as interests and style of life undergo a change.

What we have called microprocessing is accelerated by the scien­tific method. Instrument, language, and fact can relatively quickly achieve consonance, and retain that consonance unless new instru­ments or new data upset the harmony of their relationship. We have already mentioned some relevant examples. Millikan’s experiment quickly established the existence of the unit charge and the indivisible electron, and even if the exact value of that charge has shifted a little with more sophisticated techniques, the existence and approximate value of the unit charge have been established facts for nearly a cen­tury. In Latour and Woolgar’s discussion of the discovery of a releas­ing factor, the existence and structure of the factor were quickly set­tled when a method of obtaining appropriate spectrometer data was found. We have noted that Barkla’s J phenomena were not accepted because other physicists looked askance at his experimental methods involving heterogeneous rays, and preferred to develop a data domain revealed by a spectrometer utilizing homogeneous rays. A study of chemical theory culminating in modern valence theory by Gay indi­cates that the relevant data domain was discovered and stabilized by the experimental use of the voltaic pile and platinum crucibles, lead­ing to the resolution of divergent theoretical attitudes and the creation of modern chemical ideas about the bonding of molecules.³⁷ Fleck’s study of syphilis and the Wassermann reaction is perhaps the most revealing, largely because of the vagueness of the concept of a disease that can at first be known only through the presence of highly variable symptoms.³⁸ The concept of syphilis as a disease entity, as well as its relationship to other disease entities, was considerably complicated in its history by the disease’s relationship to moral attitudes about the mode of its acquisition. It is also interesting to note that the discovery of the relevant microbe did not settle the nature and existence of the disease, since the presence of the microbe is related to symptomatol­ogy in an extremely complicated way. The Wassermann test and the emergence of serology were decisive in the context of medical inves­tigation looking for the existence of blood factors. This ultimately per­mitted an intelligible relationship between acquisition, treatment, and cure to exist as a medical fact. Wassermann, of course, had not set out to find the test that has given him a place in scientific history, although he later interpreted his work as directed at that goal. The goal could not have been coherently described when Wassermann began. Fleck compares this to the voyage of Columbus, who sailed for India but discovered America. Language and reality then required (in both cases) severe adjustment. In these examples, we are con­fronted with instances of the consonance of language and fact that have remained stable since their occurrence.

It seems reasonable to conclude this section with a rather extended example of fit between instrument, domain, fact, and language that has remained stable in the face of subsequent revolution in theory. The longevity of Newton’s achievements, many of which have re­mained stable in the face of considerable elaboration, will suffice. We will take as our central example the area of physics known as classical mechanics. As originally developed by Newton, this is perhaps the first mathematical theory of nature to promise organization and expla­nation of a potentially infinite number of experimental findings.³⁹ Un­til the late nineteenth century, Newtonian mechanics was equivalent to exact empirical science. Since then, Maxwell’s electromagnetic the­ory, relativity theory, and quantum theory (among others) have rocked physical speculation, but they have not overthrown classical mechan­ics, although they have forced a much more limited view of its do­main. It is still taught to students of physics, and deserves to be taught, because it is a correct description of nature in those domains where its concepts fit facts. The newer theories belong to domains where instrumentation, fact, and theory are not consonant with classical me­chanics. They have not driven classical mechanics out of its own do­main; they show rather that classical mechanics is not viable in their domains. Heisenberg has called theories like classical mechanics closed theories.⁴⁰ They are consistent, and they are firmly anchored in data domains through appropriate instrumentation. As long as data to be described, explained, and predicted belong to the appropriate do­main, the theory cannot be improved on, and it is best regarded as true. The domain reveals an aspect of reality, and displays that aspect in a set of related scientific facts. Should not the statements fitting these facts be regarded as true of these facts? The fact that they are incompatible with the facts in other domains is independent of this judgment, as is the observation that they may not fit their facts ex­actly. With this observation the clash between the use of classical mechanics within physics and the philosophical observation that more recent theories have shown classical mechanics to be false is resolved without normative consequences for scientific practice. A similar point could be made about other domains and the languages fitting their legitimated facts. Some scientists believe that quantum theory itself is closed, and that it has adapted so closely to the relevant facts that it must remain intact within future physical theories just as classical mechanics remains intact within physical theory.⁴¹ The existence of closed theories is an important aspect of scientific progress, allowing adaptation to occur into new domains without jeopardizing the viabil­ity of theory within already explored domains. We can see it as dy­namic equilibrium achieved in the dialectic of theory and experiment between theory and legitimated fact, an equilibrium achieved where domains have remained stable long enough to permit successful the­oretical adaptation.

Theory and Experiment

In the last section we have discussed the situation that exists when a data domain stabilizes and consonance is reached between instrumen­tation, fact, language, and theory. It remains to discuss the situation that obtains when new theory or new data erupt so as to destroy consonance, or to provide the stimulus for an attempt at new conso­nance. Either theory or experiment can advance alone. When appro­priate consonance is reached, neither the addition of data text nor refinement in theory need have a catalytic influence on their relation­ship. Here we get science from science within a relatively closed do­main, theory elaborated from existing theory, or experiment from ex­isting experiment, without the necessity for constant dialectical accommodation. A novel instrument or observation may suggest a new domain, calling for novel theory, or a novel theoretical idea may pro­ject a possibly novel range of data, calling for experiment and instru­ment for confirmation. At such growth points, there may be a limited but enormously stimulating contact between theory and experiment, in which one or the other tends to define a direction of development for the other. It is at such points, where science is not developing out of known science, that external factors such as philosophical or social influences may play their most dominant role. Fixed ideas are re­quired for advance. Fleck has compared this to the motion and inhi­bition required to move a limb.⁴² Perhaps this is why the biggest moments of change may be associated with the interaction of theory and experiment, in which a fixed projection from one requires drastic accommodation from the other. During consonance, the two factors can develop more or less independently toward maximally useful ad­aptation.

We refer here to a dialectical accommodation of theory and exper­iment that is most marked during disequilibrium. Although science as a whole may show traces of this process, it cannot be expected to reach into the careers of individual scientists. Some biographies will reveal marked turns as the result of the influence of an experiment or a theoretical concept, but many will show an unyielding trajectory. The process described here will then be evident in consensus judg­ment over time, but all sorts of individual inflexibility will also be evident. This complicated relationship between accommodation in consensus and deviancy in private biography is what by now we should expect. Pushing some experimental line or theoretical bent to its ex­treme may be a necessary part of determining the significance of the ideas involved, and the evolutionary model suggests that the appear­ance of such inflexibility in the distribution of attitudes plays an im­portant role in determining the direction of group development. We can expect this feature to be most marked in physics, where the sep­aration of the role of theorist from that of experimentalist is most clearly to be discerned.

Up to this point in our discussion, we have treated data domains as though they were isolated, and as though theories adapted to them in a one-to-one relationship. It is time to examine competition between theories for domains. Two or more theories may continue in a struggle for adaptation to a domain in which consonance is not reached. If the data do not change suddenly in nature, it is to be assumed that in­creasing the data text and experimenting with theory and interpreta­tion of the data will eventually produce consonance. But it is the case that theories dependent on different concepts, such as wave and par­ticle interpretations of light transmission and electron transmission, can exist side by side for extended periods of time, each style of the­ory explaining some of the legitimated fact and predicting similar fact, but unable to deal with the entire data domain, or unable to deal with it with the accuracy displayed by the other approach with respect to some of the data. The competing theories are likely to prefer different experimental arrangements as fundamental, and to regard different selections of fact as most important in setting a theoretical treatment of the total domain. Under these circumstances, adaptation is similar to that in certain biological niches, where closely related organisms eating slightly different food and distinguished in terms of behavioral repertoire share a niche, each concentrating in numbers at its maxi­mal fit, and decreasing as one moves away from this optimal point. Its share in the total distribution may become small, but a viable variant remains ready to rush back into larger portions of the data domain should the extent or significance of the facts in the domain suddenly alter. Variants, so to speak, become consonant with parts of the domains, and are as well adapted to these parts as any theory could be. Provided that at least some significant problems depend on data only from such subdomains, the theory will remain viable, even if in this version it is not important in majority scientific discussion.

At times in the history of science, a general theory will systematize, reorganize, and provide significance for what has been a range of more specific adaptations to local data domains. The great theories—classi­cal mechanics, electromagnetic theory, relativity theory, quantum theory, statistical mechanics, valence theory, Neo-Darwinian evolu­tionary theory—have all accomplished this. In many cases, the gen­eral theory will not make exactly the same predictions from given data, or explain the data in the same way as the more restricted the­ory, but the general one has the advantage of being viable in a much larger domain than the more restricted theory. Here we encounter a point where the analogy between theory and species does not hold. Biological species consume food in order to maintain life as long as possible and to reproduce their kind. Sometimes, however, food for a species may consist of other species, as in the predator and prey relationship. Theories explain data and predict data. They do not con­sume other theories, and no analogue to the predator and prey rela­tionship seems to exist. The facts in data domains are not strictly analogous to bits of food, nor data domains to ecological niches, nor theories to species, even though this evolutionary metaphor is of con­siderable use in considering the nature of scientific knowledge and its growth over time. A theory is a disembodied set of response mecha­nisms, analogous to an organism that does not eat, but merely adapts to stimuli. It is most closely analogous to the neural adaptive capaci­ties of organisms in their response to environmental input. This is the source of value in the analogy that we have been pursuing.

Theories are strictly analogous to adaptive mechanisms that human beings can exploit in fitting and extending their ecological niche. As such, they may be compared to patterns of behavior that human beings can learn, thus increasing the sophistication of human response to stimuli. When human beings learn more sophisticated responses, their neural pathways will be altered and augmented. Theories can’t be ontologically grounded as neural pathways, since theories, along with most cultural artifacts, may exist in books, films, photographs, and other forms that are not internalized but can be consulted when re­quired by humans. Just enough may be internalized to cause the hu­man being to remember where to find help and to utilize that help. We can regard theories as extensions of human thought, just as in­struments are extensions of the human sensory apparatus. As with other thoughts, the assertions in theories will be true or false relative to their domains. Different human beings beings will have different perspectives on externalized theory, and may internalize slightly dif­ferent modes of interacting with theory. These variations, which we have come to expect, may all prove adaptive in the given data domain, while preserving alternative possibilities for adaptation in new do­mains. The final ontology of theory is as difficult as the ontology of species. It must comprise a variety of response possibilities, not all of which need be in existence, and these possibilities will share both a style and a range of stimuli. Discussion of a theory, as opposed to some individual variant of a theory, is similar to discussions in ethol­ogy of the typical behavior patterns of a species, which may not have a precise instance in any particular organism. The ontology of theories is as complex as that of many abstract objects, but we can make do by distinguishing theories in terms of their languages and assertions, which explain the response style, and the data to which they are di­rected, which explain when their response patterns will be engaged.

For simplicity of exposition, we can imagine that a scientist has internalized all the scientific theory he or she knows, so that it is all represented in his or her neural circuitry. The usefulness of storing memory and technique externally, or even its practical necessity, will then not needlessly complicate the relationship of theories. As human response becomes more sophisticated, reflex may be replaced by crude learned behavior, and the latter by increasingly refined learned be­havior. One response pattern doesn’t eat another; it can be used in­stead. This is why predacity is not a feature of theory formation. Re­flexes and cruder patterns of response may need to be replaced by more sophisticated learned behavior when anticipated results do not obtain, or when data become more sophisticated. New patterns of response obtained by practicing older patterns may call out for appro­priate stimuli. In this process of learning, the older response patterns will remain in existence. The older response patterns do match real­ity, and in at least some cases reflex may be preferable to cognition. Cognition serves to bring together data from a variety of sensory mo­dalities and test their significance against stored information and ex­istent response mechanisms. Older response patterns will remain in some form in the pathways of most sophisticated cognition, because the old pathways will have proven value in various situations. New theories contain incorporated but modified parts of older theory. The advantage of general theory is in sophistication of response to a wider possible range of data, responses being modifed by information from this wider range. Where the data are gathered by the most complex instrumentation, the wider theory will be preferable in use, and the older pathways will be circumvented.

Reduction in the philosophical sense is a way of finding formal re­lationships between theories that have received an axiomatic form. The simple historical fact is that reduction has occurred in the philo­sophical sense very rarely, if at all, in the history of science. An older theory gets incorporated, with modifications, into a newer theory, or attenuates and dies out as a response probability. For various data, two response possibilities may very nearly coincide in their anticipa­tions, but they will be different, as a reflex is from learned behavior. If data domains can be explored, extended, and carved out anew, as we have argued, then reduction to one universal theory is a practical impossibility. The goal of unified science seems to be a legacy of the­ology, and the view that there is one way the world is.⁴³ In theology, God is sometimes said to have created the world according to a blue­print, which, if it could be known, would explain the precise structure and workings of the world. The idea that physics, in pursuit of the smallest constituents of reality, is uncovering the fine-grained blue­print, while the methods of other sciences provide convenient short­cuts, appears to be the descendant of this outlook. In the view offered here, the complexity of reality defeats the unified science hypothesis, although the drive for more general theories remains a desirable as­pect of scientific motivation. Different sciences will offer different mo­dalities of interaction, all of them equally legitimate. This does not cut against, or for, religion, since God can be imagined to have cre­ated a world not fully within His rational grasp, although this requires some adjustment of the concepts of His omnipotence and omnisci­ence.⁴⁴ The most frequently cited reduction in scientific history, that of phenomenological thermodynamics to statistical mechanics, illus­trates our claims. As is well known, the temporal asymmetry of phe­nomenology disappeared in this reduction, even though many of the other statements in phenomenological thermodynamics were taken over wholesale. This is the pattern we expect. A new theory will incorporate major features of older theories, but it will modify some features in extending its applicability to a wider domain of data.

Let us consider a new data domain, perhaps one being explored with new instrumentation. At first, older theoretical responses will be tried. If the older responses are not adequate because they do not fit the structure of the data, or are predictive of nonobserved data, they will typically be modified by mixture of older response types. This is similar to biological adaptation from existing stock. Some lucky mu­tation can occur that is advantageous, but the standard method of adaptation is to shuffle existent genetic possibilities in new combina­tions. (This shuffling, of course, constantly goes on, but it doesn’t shift distribution of genotypes dramatically in a fixed environment.) New data are always both like and unlike existent data in an infinite num­ber of possible ways. The yardstick for its evaluation must be existent language if chaos is not to reign. Goodman proposed that entrenched classes of objects be used to project new data as a way of avoiding predictive chaos.⁴³ This proposal deals with the problem of induction by arguing, not that the relationship of past to future can be guaran­teed in methodology by accepting that theory most likely to be true, but that we always try existing projections until they encounter diffi­culty. Holton has suggested that scientists theorize in terms of the- mata, that is, in terms of a set of ideas that are highly adaptable to data, such as viewing various entities either as waves or as particles, and so on. These concepts, which have a long history in our thought patterns, can be reshuffled and refined to produce a new theory when data so demand.⁴⁶ Holton’s view allows new theory to arise from crossbreeding between older theoretical conceptions, and permits an extension of Goodman’s idea to situations with complex conceptual antecedents and to situations in which divergence between theoretical outlooks is possible. According to both of these accounts, new data do not create new theory; they create primarily reshuffling of existent theory to find a new language. When this process leads to a quite new language in a short period of time, a revolution may seem to have occurred. When a domain is rapidly expanding, divergent theories or research programs may be simultaneously progressing, just as rival colonizing species may all be increasing in number in a new ecological niche. The mere fact of progress in solving problems and accommo­dating data may not be an indicator of eventual success. As we have noted, rivalry may exist for a long period of time, or be terminated by extension of data text or the production of a more general theory. Many commentators have noted the widespread appearance of anal­ogy and metaphor in scientific understanding. From the prospective suggested here, analogy and metaphor are the mechanisms by which the style of older theorizing is extended to new domains, and the two would be encountered wherever data are causing theoretical read­justment.⁴⁷ The much discussed simplicity of nature may be the re­flection of the fact that reshuffling of theory has proved such a suc­cessful strategy to date. New data domains have always yielded to a similar means of theoretical extension.

In the biological domain, reshuffling of genetic material is primarily the result of a random or pseudorandom process in meiosis. If meth­odology could be made explicit, or there were an inductive logic, no room for reshuffling would be available at crucial junctures. In sci­ence, the fact that individual scientists vary in personality, aesthetic vision, and so forth provides room for a variety of possible reshufflings of existent theory (and allows key mutation), the better variants of which process will be determined by group interaction with the rel­evant data domain. One method of extension can be to reevaluate existing theory and to find a general theory that fits the important cases in existing theory, although it condemns other data to the status of being wrong or irrelevant. Newton, in generalizing from Kepler’s laws, took them to be important in a way that neither Galileo nor Descartes could have, in view of their settled interests in the Co­pernican and vortex theories.⁴⁸ In adding the notion of mass to that of inverse attraction, Newton was able to incorporate slightly altered versions of Kepler’s laws in his theory, while decisively repudiating versions of facts accepted by Galileo and Descartes. Another method, particularly in the case of complex data, is to allow an image from common sense to organize the data until a mathematical refinement makes scientific sense. Gruber has shown how the image of a branch­ing tree allowed Darwin to suspect a pattern behind the complex data of breeder’s observations, and so on, until a suitably precise scientific form of that image could be constructed from existent concepts.⁴⁹ In this image, there is continuity in branching, but the termination of a branch marks cessation of growth in that area. Extinction of possibil­ities is thus required if the total number of existent organisms is not to grow beyond observed limits. Much of the imagery to be made precise in the theory of evolution is contained in this general image. Wise has shown that an image of similar generality, consisting of elec­tric and magnetic current as represented in a pair of interlocking rings derived from Faraday, guided Maxwell’s development of the mathe­matical description of the interrelation of electricity and magnetism.⁵⁰ In order to consider the reshuffling of themata along the lines sug­gested above, we can turn briefly to the history of quantum theory from 1913 to 1927.

The development of quantum theory from 1913 to 1927 not only shows reshuffling of themata, but also shows how different scientists attacking the same data may piece together different theoretical ad­vances by means of choices among existing possibilities.⁵¹ In this proc­ess, the visualization of nature’s structure that classical theory allowed was destroyed, and then regained as the fit of quantum theory to the data allowed scientists once again to feel that they could see structure by means of their theory. In 1913, Bohr proposed a new theory for the classical atom that retained Rutherford’s picture of the atom as a miniature solar system, but involved open conflict with classical phys­ics in its consequences. Through a series of small steps, Bohr was forced to yield Rutherford’s picture while adopting a nearly incom­prehensible theory welding both continuous radiation fields and dis­crete particles of matter into an explanatory apparatus for the accu­mulating data. In the ensuing development of theory, choices had to

be made between the themata of continuity and discontinuity, wave and particle, causation and noncausal “jumps,” and between mathe­matical models of process with an uncertain relationship to reality and more familiar mechanical models. By mid-1925, Bohr and Heisenberg were forced by their interpretation of data and choices in favor of discontinuity, particles, noncausality, and mathematical models to de­velop an essentially unvisualizable mathematical model of quantum processes to fit the important experimental data. In 1926, Schrodinger made choices in favor of continuity, waves, causality, and realizable models, and developed a wave interpretation of the same phenomena while stressing slightly different experimental data. Shortly there­after, a somewhat eclectic interpretation was developed by Born in which the particles were seen as guided by waves, and partial visu­alization was restored. Controversy between the various theoretical outlooks, with unmistakably fruitful consequences for quantum the­ory, was partially resolved by the discovery that wave and quantum mechanics were essentially intertranslatable pictures, allowing one or the other to be used in conformity with the needs of any special prob­lem and the expertise of the individual scientist. In 1927, Bohr pre­sented a theory that resulted in the so-called Copenhagen interpre­tation of quantum theory, which a majority of physicists soon accepted. The particular example of quantum theory shows that alternative shuf­flings can lead to equally adapted forms of theory. In other cases, of course, nonequivalence of reshuffled theory will lead to a markedly skewed distribution of individual interpretations in the light of ev­idence.

To this point, we have viewed new data as the primary motor of scientific development, and we have examined possible lines of the­oretical adaptation to new data. In order to sustain a dialectical inter­pretation of progress, it is also necessary to consider the way in which new theory can force a recognition that new data are requisite. The most obvious mechanism for this is well known. Development of an existing theory can lead to the anticipation of data to test its fitness. The discovery of Neptune and the discovery of the positron are ex­amples of this mechanism, involving somewhat different levels of data augmentation.⁵² Existing theories can also be discovered to conflict with future data when they are developed, thus leading to the possi­bility of an experiment that can decide between them. A more inter­esting development is when theoretical reshuffling produces such a conflict, a situation that can prove stimulating to experimental devel­opment. An interesting example of this phenomenon is the contro­versy that raged in cosmology for some time between steady-state and evolutionary models until the data produced by the debate settled the controversy pretty much in favor of evolutionary models. In this case, the steady-state theory was produced, not by new data, but by a new interpretation of data in which theory was reshuffled because of con­sideration of the philosophical principle that the universe must be the same in its major features as one journeys out from our viewpoint in space and time.⁵³ Since local data would be equivalent on the two theories, it was necessary to invent new experimentation in the hope of adjudicating between them. In this case, of course, the theories did not turn out to be equivalent, and one of them had to give way.

The fact that some theories can replace other theories, or eliminate them from science, may seem incompatible with the idea that any theory that achieves community acceptance at some time in the de­velopment of science captures an aspect of reality. Phlogiston theory and steady-state theory did capture aspects of reality, but we regard them now as false because their explanatory claims diverge from fact in later, expanded data domains. As chemistry and astrophysics de­veloped, the explanatory capacity of these theories lost out to superior alternatives. What they tell us of reality is therefore partial, and there is no reason not to call them false in the wider domains. At the same time, classical physics and static earth astronomy are still taught and still used, even though they have given way to other theories in ex­panded domains. Why are these different? Why are they still consid­ered true, even if only in these restricted domains? Because the do­mains to which they adapt still retain an identity in science because of their close relationship to ordinary naked eye observation and pur­poses related to this fact that remain essential for human beings, such as the construction of machines and the navigation of boats. There must be both a separate data domain and an ongoing purpose for this domain if an older theory is to be retained and taught. If the wider domain to which relativity theory adapts had not been developed by new instrumentation, classical physics would still be adequate. The slight theoretical superiority of prediction of relativity theory within the domain of classical physics is compensated for by a more compli­cated and inaccessible mathematical apparatus. But since both are well adapted to the restricted domain as developed by the appropriate instrumentation, neither need force the other out. In the case of phlo­giston theory, by contrast, new chemical data gathered by essentially the same sort of chemical experiment eroded the boundary and the legitimacy of the domain to which phlogiston theory had adapted. The ontology of rejected theories in larger domains is thus sensitive in its ongoing acceptance to the details of development of data domains and the continued usefulness of relatively natural domain boundaries. Our normal discussions of the truth or falsity of theories would need to be brought into coincidence with the historical details of domain enlarge­ment and discovery of new domains, but the rather abstract treatment here gives promise that these accommodations can be achieved with­out violence to scientific intuition in specific cases.

Besides predicting new data, theory shift can cause a reinterpreta­tion of older data, which in turn can stimulate the search for new data. One amusing example of this began with Thomas’s nearly acci­dental discovery that injections of a substance called papain uniformly caused the ears of experimental rabbits to droop, a striking and reg­ular change.⁵⁴ His examination of the cells of the ears of the injected rabbits showed no abnormalities, and he was unable to find an expla­nation. This experiment arose in the context of another line of in­quiry. Some years later, when Thomas was teaching pathology, he showed his students the effect of the drug, and then examined the tissue of rabbits who were and were not injected. In this circum­stance, the fact that gross quantitative changes in cartilage cells had occurred was obvious, even though none of the cartilage cells by itself showed abnormalities. This experimental discovery changed the prior theoretical opinion that cartilage was inert tissue and played no role in physical reactions. We see here how an observation in the right theoretical context can run counter to the theoretical background that would otherwise constrain its interpretation.

Another interesting example of theory shift causing a new interpre­tation comes from medical history.⁵⁵ At the beginning of the nine­teenth century, scurvy and rickets had been discovered to be diet related, and dietary cures for the diseases were well known. In the historical context, the diseases were consequently thought to be understood. During the nineteenth century, the development of the germ theory of disease promised a universal explanation of disease as the result of infection by microorganisms. About 1880, beriberi began to be of interest to Western doctors. The fact that beriberi could be contracted by persons eating a wide variety of foods, that those who contracted beriberi might be on a poor protein or high protein diet, and other observations, convinced most Western researchers that the disease was not related to diet. Researchers looked for a microorgan­ism as the causative agent. The breakthrough observation was that consumption of polished rice was responsible for a similar disease in chickens. In the new setting, the connection between polished rice and beriberi was not viewed as giving an understanding of beriberi as the connection between the absence of certain fruits and scurvy had done for scurvy earlier. If the polished rice did not cause beriberi through connection with a microorganism, it was necessary to find the factor (nutrient) whose absence caused the disease. In the new con­text, it became clear that the nutrients essential to health had not been purified and identified, and that this had to be done in order to understand deficiency diseases. Thus the existence of the germ theory gave the facts concerning diet and beriberi a new significance, and led ultimately to a modem deficiency theory of disease.

The result of this survey has been a welter of possible mechanisms for dialectical accommodation of theory and experimental fact. Exper­iment can lead theory, and vice versa. We should not be surprised to find that very complex interactions between new theory and new ex­periment are possible, ruling out any methodology based on either inductivist or deductivist proclivities. There can be no a priori mech­anism for advance. One will have to be sensitive to the details of particular cases and the facts of any scientific setting. In order to clinch this observation, three detailed studies of scientific history of more than passing interest will be briefly described and commented on.

A study of the discovery of Boyle’s law will constitute the first ex­ample.⁵⁶ Boyle’s law was gradually formulated during a complex in­teraction of philosophical theorizing and experimental development in the seventeenth century. The interest of this case is that it stands on the borderline of an emerging scientific discipline where prescien- tific concepts play an important role and no settled experimental strat­egy is recognized. A flurry of European experimentation on the elas­ticity of air occurred from 1640 to 1650 as a result of a philosophical controversy between vacuists and plenists. Vacuists utilized the an­cient intuitions of the atomists that motion was possible only if atoms could move within a void. Plenists owed their views to Aristotelian arguments against atomism, which asserted, among other things, that bodies passing through a void would all move at the same rate (indeed instantaneously), contrary to the observed difference in velocity be­tween light and heavy bodies. When water was boiled and turned into steam, Aristotelians viewed this as an expansion of matter, which produced rarefaction, but not a void. Remnants of this dispute appear later in the quasi-philosophical arguments of Galileo, Descartes, and Newton. The consequence of this theoretical dispute was a series of attempts to produce a vacuum, the centering idea of which was to fill a tube closed at one end with water, to invert the tube in water, and to note that a space appeared within the tube over the water. If there was now nothing where there had been water, a void had been cre­ated. These early experiments were ambiguous because of the chang­ing height of the water column, strange sounds observed during the formation of the supposed vacuum, and the embarrassing fact that the vacuum produced seemed to transmit light, magnetism, and sound. A series of counterexperiments was then located, attempting to prove that air (unlike water) was indefinitely elastic. In one such experi­ment, a carp bladder was inserted into a tube closed at one end and filled with water, and when the bladder was surrounded by the space over the water in the inverted tube, it expanded greatly (like a bal­loon), showing that a fixed quantity of air could fill a space of varying dimension. Needless to say, these experiments could be defended and attacked by both sides of the philosophical dispute in spite of efforts to obtain an unambiguous experiment to end the series. Here we have a very complicated interplay between rival theory and experi­ment.

Before long, the experiments referred to, largely conducted in France and Italy, had engaged the attention of British and German scientists. In England, Boyle constructed a pneumatic engine designed to pump air out of a container whose interior could be studied by various in­struments. This sharp increase in instrumental sophistication was cou­pled with skepticism concerning the plenist and vacuist controversy. Boyle suspended judgment, thinking that neither side possessed a true physical description of air. A new series of experiments was then realized, for example, some experiments in which the density of air in the container, as measured by piston travel in the pneumatic en­gine, was plotted against the elasticity of air, as measured by the height of a mercury column it could support. Even prominent math­ematicians could find no simple correlation, for the unknown fact was that the container leaked, and leaked worse as it was exhausted of air, and so the mercury column could not be accurately calibrated. An­other series of experiments, performed by a variety of investigators but marred again by primitive equipment and uncertain calibration, did establish the diminution of atmospheric pressure with increasing height above sea level, a fact related to the elasticity of air. Not all of these experimenters followed Boyle’s caution in evaluating the phil­osophical arguments. Boyle returned triumphantly to the disputes by adapting a siphon into a J tube, in which a short sealed arm containing a quantity of air could be balanced by a column of liquid in the long arm. The apparatus was troublesome, since accurate data required a uniform bore in the tube, a seal that would hold under pressure, and arms so long that they were subject to breakage. Yet in this new apparatus, volume of air (as opposed to density of air, the older con­cept) could be measured against pressure (as gauged by the height of the balancing liquid column). With this apparatus, as well as another piece of converted apparatus, Boyle gradually accumulated the data necessary to advance the conjecture bearing his name, although his perception in his philosophical milieu differs somewhat from our per­ception.⁵⁷ This example shows several interesting features, as Webster points out. Originally, theoretical dispute (albeit partly philosophical) controlled the direction of experimental research. Group enterprise and communication were essential to the development of suitable equipment and experimental technique. Boyle’s discovery, although anticipated by others, was grounded in his case in superior apparatus and suspension of belief about theoretical attitudes. Boyle’s law is an experimental discovery of considerable magnitude, since it is perhaps the first of the modern functional equations, in which reciprocal causation occurs between related variables, a change in either result­ing in a calculable change in the other.

The next example is a study of the rise of valence theory in chem­istry as a reshuffling of the themata of the radical and type theories that had preceded it.⁵⁸ This period of chemistry lasted from approxi­mately 1830 to 1860. It begins with the discovery of the voltaic pile, an instrument that could be used to decompose chemical compounds. The electrical nature of the decomposition led to the proposal that every compound substance was composed of an electrically positive and an electrically negative part. These parts were the so-called rad­icals of radical theory. Radical theory was able to decompose all sorts of inorganic compounds, but there were anomalies. On the one hand, the same radical (chlorine, for example) might be a positive radical in one compound and a negative radical in another. The theory had to be sufficiently complicated to deal with these data. Further, organic compounds composed of large numbers of the same elements couldn’t be conveniently divided into radicals, and sometimes couldn’t be de­composed at all. Here we have the discovery of new apparatus giving rise to a new and quite general chemical theory. As electrochemical explanation failed to provide an explanation of the structure of com­pounds in all cases, type theory began to develop in which chemical reactions were used to organize compounds, those compounds partic­ipating in analogous reactions being regarded as of related type. The chemical character of a compound is thus to be related to the number and arrangement of its constituent atoms. Water, which binds an H (hydrogen) to an O (oxygen) and an H, is of a similar type as ethanol, which binds a C₂H₅ to an O and an H.

Clearly, both radical theory and type theory were able to organize and explain a great many isolated chemical facts, and adherents of both theories were successful in guessing the number and nature of the atoms constituting certain important compounds. The gap be­tween data and theory here is enormous, since most chemists as­sumed in the nineteenth century that the internal structure of mole­cules could never be directly observed, partly because of the apparent limits of microscopy. Both radical and type theory were progressive at this point, producing detailed experimental data and fitting them into conceptual schemes. It was, however, increasingly evident that both the number and arrangement of atoms, as well as their electro­chemical nature, were involved in chemical structure, and that this complex fact had to be incorporated into the study of organic com­pounds. In 1858 Kekule effected a reconciliation of the two theories. Kekule began to take formulae as pictures of the structure of com­pounds, and not just as a record of the input and output of reactions. Radicals remained as groups of atoms not affected by certain reac­tions, and as structures (types) that could play a role in other reac­tions. His resulting formulae were a huge advance, and his recogni­tion of carbon-carbon bonding represented a huge step toward an understanding of organic chemistry. Like the development of quan­tum theory mentioned earlier, we have in this case the stimulus of new experimental data leading to rival theories that are resolved in a successor theory. Unlike the case of Boyle’s law, the general direction here is from experimental data to theoretical accommodation of large scope, a pattern frequent in historical chemistry. An interesting fea­ture of this example is that neither radical nor type theory was falsified or degenerating when each was overtaken by valence theory, nor was valence theory the result of revolution in that it resulted from the crossbreeding of prior theoretical ideas along with the somewhat mu­tant idea of carbon-carbon bonding, which may have been suggested partly by the discovery of gas molecules to be found in an uncombined natural state.

The third example to be considered here is the overthrow of parity conservation.⁵⁹ This example from twentieth-century physics is inter­esting because it illustrates the distinction in role between the exper­imental physicist and the theoretical physicist. Perhaps because of the severity of this functional split, besides the experimental and theoret­ical papers of modem physics, one can identify phenomenological pa­pers that build mathematical models of selected experimental data, so that data and theory are more easily related and accommodated to each other.⁶⁰ The history of particle physics of concern here extends from 1950 to 1970. At the start of this period, experimental and the­oretical activity were relatively independent. In 1952 and 1953 a puz­zle emerged from experimental data that was an extension of previous experimental design. The decay of a certain meson (a positively charged particle) seemed to lead to two possible outcomes, a result suggesting that there might, in fact, be two different particles. While experimen­tal evidence accumulated that there was only one particle in terms of mass and lifetime, a phenomenological argument was produced show­ing that if parity was preserved, the two decay modes meant that there were two particles. By 1954, theorists had become embroiled in the question of whether there were or were not two different par­ticles. In 1956, Lee and Yang produced a theoretical argument ques­tioning the existence of parity conservation, and pointing out that its conservation in the relevant context was not well supported by evi­dence. They proposed several experiments to settle the matter, and this stimulus provoked new experimental activity that demonstrated parity nonconservation within a few months. This, in turn, triggered intense theoretical activity designed to explain parity nonconserva­tion. The V-A theory of weak interactions was proposed by Feynmann and Gell-Mann in 1957, a theory rich in deductive consequences sub­ject to experimental test, and this challenge was accepted by experi­mentalists. Partly because of the separation of roles in physics, this example shows how complicated the interaction of theory and exper­iment can be over a short period of time. There is at first independ­ence, followed by an experimental result that provokes new theory, after which theory leads its experimental testing. The relationship could hardly be more complicated, since all of these events take place in about a five-year period within one specialty within physics.

In addition to the criticisms that have already been offered of the nondialectical accounts of scientific progress in earlier discussion, it is clear that these accounts cannot survive a budget of detailed historical examples, or even the three examples that have just been discussed. Gay remarks directly that her account of chemical history is incom­patible with Lakatos’s methodology of research programs in that rad­ical theory and type theory were both progressive when they were overtaken by valence theory, and White, Sullivan, and Barboni re­mark that their account of particle physics history is also incompatible with Lakatos’s methodology in that particle physics seems intuitively to have been progressive even when its excess empirical content was declining.⁶¹ In the work of Popper, Kuhn, and Lakatos, there is a tendency to suppose that theory must control the direction of exper­iment, and that history revolves around the relationship of theoretical structure to data. All three examples we have looked at exhibit pe- nods of scientific investigation in which experiment is directing the­ory, and situations in which the significance of data is determined to be at odds with the prevailing theoretical climate. If theory and ex­periment can be separated as the moments of scientific progress for analytical purposes, the extant philosophies of science have confined themselves largely to the development of theory to the exclusion of experiment. Even Kuhn, whose descriptive account seems most eas­ily to conform to scientific practice, has missed this division of labor, and seems not to have dealt with the fact that only some anomalies will be seen to be significant to theory, and to cause its reshuffling. The dialectical account attempts to redress this imbalance, and to relate theoretical evolution to instrumental development and the per­ceived significance of data. It could be embarrassed by an adequate methodology constructed along nondialectical lines, but none exists, and none seems to be in sight when the complexity of detail as a result of the burgeoning history of science is confronted. This particular di­alectical account would also be embarrassed if better history indicated that the direction of evolutionary development and the extinction of theory were not clarified by apposite studies of instruments and ex­perimental design, and in the process rendered less dependent on postulated genius. Except for this constraint, the dialectical view we have developed places almost no theoretical restraints on scientific history, and encourages involvement with the details of scientific sit­uations without preconception about the role of theory or experiment in influencing the other.