SCIENCE AND NONSCIENCE

Science and Pseudoscience

In the last two chapters, we have considered some philosophical and sociological attempts to capture the essence of scientific practice. It has been argued that these attempts have failed, and this chapter will propose that there is good reason for this failure.

Let us begin with a consideration of parapsychology. Parapsychol­ogy is not regarded as a scientific discipline in many quarters, but how can it be ruled out as a scientific discipline? It is surely not the case that all orthodox scientists reject parapsychology, since many or­thodox scientists have come to accept at least the possibility of para­normal phenomena, even though they may not themselves be en­gaged in research on the paranormal.

Criticisms of parapsychological research have not produced a sci­entifically respectable alternative theory to account for the experi­mental results. The critics may hint darkly of fraud, although fraud discovered in a legitimate field does not count against the legitimacy of the field, or they may suppose that there is always an explanation within the framework of orthodox science for nonfraudulent results.

The attempt to differentiate science quite sharply from nonscience is usually set against a dispute between science and something not considered to be science at all. Some might wish to rule parapsychol­ogy out completely as a possible science, and would welcome a rigid philosophical boundary around science. What is not so frequently considered is that if scientific practice inside major scientific disci­plines breaks down into small research groups, some of these will strike off on the pursuit of schemes that will seem wild to their con­temporaries in the same discipline. Some of these adventurous sallies will revolutionize science. A basic point is that many of the most revolutionary new theories introduced historically into any scientific disciplines were at first regarded as completely wrong by contempo­raries. All of this suggests that we don’t want a sharp boundary around what counts as science, or that such a boundary serves no really useful purpose. It is impossible to tell of fledgling disciplines whether they are or are not scientific, or whether they will or will not be absorbed into recognized disciplines, or even create new ones. Such judgments come later. Clearly, there is a difference between central scientific disciplines and nonscientific disciplines, and we want to be able to understand that difference even if we can’t draw a clear borderline between them. This situation is like that of the difference between being alive and being dead. There are creatures that are clearly alive and creatures that are clearly dead, and the difference is of consid­erable interest to us in many cases. This difference is not obliterated by the fact that it is difficult to define alive and dead so as to provide a criterion for adjudicating all cases. The positivists wished to provide a normative paradigm of good scientific practice and to draw a clear boundary between science and nonscience. The latter was undoubt­edly a mistake.

What may at first seem surprising to those who are captured by the idea that a boundary between science and nonscience can be drawn in principle is that claims within orthodox scientific disciplines may be rejected by the majority within the discipline, and that this rejec­tion may be defended by invoking dubious methodological criteria. The problems encountered concerning parapsychology and orthodox psychology may be played out entirely within an orthodox area of science. A scientist’s work along orthodox lines may be rejected for reasons that seem merely to gloss rejection, and not to express legit­imate causes for rejection. British physicist C. G. Barkla won a Nobel Prize in 1917 for his discovery of a set of X-ray emanations from atoms in the so-called K and L series.² Prior to his acceptance of the Nobel Prize, Barkla had also announced a J series of emanations, at first accepted by others on the strength of Barkla’s reputation, but then regarded by most physicists as a derivative phenomenon that could be explained by the widely accepted Compton effect. Barkla’s exper­iments, including those that had produced the K and L series, focused a powerful heterogeneous high-intensity beam of X-rays onto various atoms. The J series phenomena were a natural methodological exten­sion of the earlier experiments at a higher beam intensity. Other physicists, including Compton, were attracted to a new instrument, the spectrometer, that produced X-ray beams that were of the same wave length, but much less intense. Barkla’s and Compton’s theories are not in direct opposition, since they were invoked to explain data deriving from different experimental arrangements. But in this dis­pute, Compton sided with orthodoxy in quantum theory (and helped to develop that orthodoxy), while Barkla opposed various features of the orthodox quantum theory. Barkla admitted to error on the original J series, but adopted a new view about related J phenomena, which were taken by him to be organic or emergent properties of hetero­geneous radiation, properties that could not be discerned in the single wave-length spectrometer of the Compton experiments. Barkla’s op­position to spectrometer experiments was methodologically subtle, centering around the idea that low-intensity experiments might fill in a certain amount of detail, but couldn’t lead to fundamental new dis­coveries. Thus Barkla does not represent conservatism, even if this theorizing was in terms of an older language, but rather an attempt to go beyond what he saw as the instrumentalism of quantum theory to a more realistic and comprehensive physical theory. Nonetheless, by 1923, Barkla was literally alone as an exponent of the absorption experiments he had pioneered, and he is often pictured as an eccen­tric crank in his later years, even though he attained many honors and still published frequently. Papers were published allegedly refut­ing Barkla, or repeating his experiments with homogeneous rays and announcing the discovery that Barkla’s data could not be obtained with such rays. The latter is hardly an objection, since Barkla re­garded heterogeneous rather than homogeneous rays as a cause of the organic mode of data that he sought. Barkla placed sixteen advanced degree students for J phenomenon work between 1924 and 1945, even though most orthodox scientists thought the work to be nonsense.

What is interesting about this case is that it is a case where nonsci­ence or pseudoscience as judged by peers develops within an ortho­dox scientific community and is accommodated within that commu­nity, even though it is recognized as deviant. Barkla’s J phenomenon can’t be ruled out as nonscience in terms of methodological criteria, since it was developed as a smooth methodological extension of Bark­la’s previous science. It just happened that most physicists took the alternative path of using the spectrometer. One can suspect that Bark­la’s organic theory violated a very general value of physics concerning the analytical approach, that is, the value of the correctness of analyz­ing something into its constituents, where possible, for the purposes of understanding. Thus most physicists probably regarded the homo­geneous beams as a more basic and potentially useful exploratory tool than Barkla’s heterogeneous ray. But this analytical preference can’t be refuted by logical or even methodological objections alone. There­fore, our second case is like the first in suggesting a community of scientists who have internalized various values whose violation nor­mally entails the sanction that work performed under the violation is regarded as nonscience, and may be largely ignored by other scien­tists.

An important aspect of the Barkla case is that one and the same scientist engaged in both orthodox and deviant science. It is hard to credit the possibility that he was schizophrenic, or that in some other way his mind was clear only when he was doing good science, but was confused when he was doing bad science. Such examples tend to show that good science can’t be separated from bad science merely by the logic of situations. Paradigmatic values shared by some group seem to be involved in distinguishing good science from deviant sci­ence or even pseudoscience that is pursued according to sound meth­odological principles, that is, the same principles that seem to char­acterize good science. A second example may help to underscore the importance of this point. As is well known, Pasteur did early crystal­lographic work on tartaric acid, work designed to connect the crystal structure of these acids with their optical properties.³ One acid that did not rotate polarized light, for example, he discovered to have symmetrical crystals, while another acid that did not rotate polarized light he discovered to have left- and right-handed forms, which when mixed in equal amounts in a solution seemed optically inert. These discoveries completed a research program that had been begun by the French scientist Biot some forty years before Pasteur’s work. Pas­teur’s work depended on the microscope and the goniometer (used to observe crystalline forms), and was quite in line with the traditions that had studied, for example, the optical properties of quartz crystals. After Biot was convinced that Pasteur’s work was correct, his support in the Academy of Sciences led to the rapid dissemination and ac­ceptance of Pasteur’s discoveries. But then Pasteur pushed on to greater generalization. He attempted to link crystalline form to properties of living things and even to the universe. He began to bathe plants in unnaturally polarized light, and used magnets to attempt crystalline distortion. Pasteur’s new problems were deviant, and his methods unorthodox. But he was not mad. His fellow scientists, worried about the effects of such experimentation on his career, helped to move his interests in the direction of problems of fermentation, where he made discoveries of fundamental importance.

Clearly, although the existence of paradigmatic values is an impor­tant feature of scientific practice, and helps to explain the reaction of orthodox science to deviant science, the existence of such values alone will not differentiate good scientific work from deviant work or even sophisticated pseudoscientific efforts. The context of such values helps to explain why some science is regarded as deviant at a particular point in time, and to define orthodox practice. At the same time, it is possible to recognize scientific practice in the work of pioneer sci­entists who do not share the same paradigmatic values that are shared by other scientists in a recognized field of science. These scientists may be creating new fields of investigation, and their work need not be based on a perception of anomalies threatening some existing line of research. Galileo can furnish a sufficient example.⁴ Groups sharing paradigmatic values are typical of modern science, as in Kuhn’s con­ception, and perhaps the existence of such groups is required to deal with the distinction between orthodox and deviant science. At the same time, such groups do not need to exist for science to be prac­ticed, for science was practiced early on in the absence of such groups and is practiced by many pioneer scientists as an individual activity. What the individual scientist within or outside such a group succeeds in doing is to narrow down complex and confusing data and observa­tions into a manageable domain, often defined by the data that can be gathered by various instruments. Different individuals can then know that they are investigating the same data in the same manner, and scientists can recognize the relationship of new work to older work that had been done previously in the same domain. Science carves out, so to speak, something akin to immanent Platonic ideas or Aristotelian forms from the world and studies their instances. Physics and mathematics show this feature quite clearly. The same numbers and electrons have been available to all mathematicians and physicists for study. Recognized groups help to define common problems and techniques, but they are not necessary, even though they are perva­sive in modern science and essential to the dynamics of its develop­ment. A pioneer scientist, once again, may propose important new scientific information without immediate group support. Because of this, mere perceived deviancy at some time, even deviancy perceived by some relevant group of orthodox scientists, cannot be taken as a criterion that the deviant scientific practice is not sound.

The move to science from nonscience or pseudoscience is the move to relatively simple questions put to nature through experiment that have widely recognizable answers. Scientific questions are designed to find out how nature works, what reality is like. And as Chapter 1 suggested, reality is like the picture that the sciences develop, al­though it is also like other pictures. The move to science may be perceived in the triumph of medicine over astrology.⁵ Before 1700, it would have been difficult to defend the record of medicine over that of astrological practice, since medical treatments, for example, bleed­ing and purging, were frequently harmful. Astrological practice may actually have been more frequently beneficial because of its nonma- nipulative therapeutic practice. Medicine, however, gradually organ­ized and achieved fixed levels of practice, both of these achieved in England, for example, through the formation of the Royal College of Physicians and its sponsorship by the crown. Medicine gradually con­trolled its patients through its determination of which sorts of medical questions could be asked, and what sorts of answers were permissible. Medicine also developed instruments to assist in asking and answering questions about a patient’s body independently of the patient’s opin­ions. Astrology, on the other hand, was ad hoc and problem centered, responding to whatever questions were brought to the astrologers by those seeking them out. As the grandiose claim of astrology was that everything is determined by the stars, there was no reason for astrol­ogy to appeal to instrumental limitations in blocking lines of inquiry suggested by certain questions. And as the astrologers were an amor­phous lot, consisting literally of all those calling themselves astrolo­gers, fixed questions and agreed-upon answers to them were not de­veloped by an astrological society, and patients could get quite contradictory information by consulting various astrologers utilizing divergent astrological systems. Medicine gradually came to dominate nature, seeking answers to aggressive medical questioning through experimentation, and attempting to control the course of nature through a manipulative therapeutic practice. The victory of medicine over as­trology for the status of orthodoxy is symptomatic of the development of science in comparison to pseudoscience. Both science and pseu­doscience may be theoretical, and both may experiment. Science, however, simplifies the nature and range of questions to be asked of nature in a direction that promises answers to the questions, answers that many may study through appropriate experimentation with or­thodox instrumentation. Medicine can admit to being stymied by a wide range of apparent illnesses, but it has standard and recognizable diseases and standard treatments for them. Medicine, in other words, observes the course of a specific illness in a specific person and sug­gests a specific treatment. A course of study was developed that placed this practice within the orthodox educational system. Astrology seems to have been unable to make these adaptive moves. Its treatments and questions remained too general. Persons could be grouped to­gether by the heavenly configurations at the moment of their birth and then treated alike, but the groups have seemed so heterogeneous that various astrological theories concerning such groups remain in a competition that cannot be settled by appeal to common paradigmatic values and an agreed-upon experimental and instrumental practice. Whatever scientific truths exist in astrological practice, if any, they remain obscured in a sea of conflicting seers’ opinions.

It has been suggested here that orthodox science and deviant sci­ence cannot be differentiated by methodological criteria or by refer­ence to a generalized group structure. What seems to be the case is that a scientific field is created when a limited set of questions about reality is formulated and can be put to nature through experimenta­tion with the hopes of receiving definite and repeatable answers. Fur­ther, orthodox science develops over time in the direction of refine­ment of the questions and the experimentation for answering them, whereas deviant science seems over a period of time not to develop in this direction. The general problem for any absolute separation is that what is deviant at some time may develop later into orthodox science, particularly since nascent fields are so often perceived as de­viant by existing orthodoxy. There is no general method for differen­tiating science and nonscience, or for branding deviant science as non­science. We have to look for history to make these determinations, and that always both provisionally and from a point of view in histor­ical time. Deviant science may grow into science, make discoveries that contribute to later science, or provoke the growth of genuine science. This fact cannot remain mute within any philosophy of sci­ence attempting to deal coherently with scientific progress.

Science and Society

We have seen that many philosophers of science have attempted to construct a sharp conceptual boundary between science and nonsci­ence, where nonscience is interpreted as nonscientific intellectual ac­tivities. In this chapter we will consider some related boundaries pos­tulated to exist between pure science and applied science and between science as an institution and other social institutions. Where nonsci­ence was in question, the major point of a boundary seemed to be that only science could lead to knowledge, whereas nonscience gath­ered and organized mere prejudice or dealt with fictions. The effort to separate pure science from technology and societal influence is slightly different in tone. Here the effort seems to be that science gathers disinterested knowledge, or objective knowledge, whereas technology applies this pure knowledge to ends chosen by industry or by the interests of some segment of society. Whatever pure sci­entists discover need not be discounted for personal prejudice or for subservience to nonepistemological interests.

The philosophical attempt to distinguish pure and applied science is perhaps also related to a familiar philosophical predilection to favor pure thought, in other words, to a philosophical predilection to favor activities similar to philosophical activities. Philosophy in many of its historical forms has been dominated by a quest for certainty, a quest for permanent knowledge, and the philosophical picture of science tends to be of one piece with this attitude. According to some philos­ophers, pure scientists may be construed as calculating the values of various theoretical functions on data values obtained by careful ex­perimentation. For these philosophers, the ideal scientist deals solely with facts and calculations, and cannot make any other than a com­putational error.⁶ Good scientific practice then exists on a plane that is literally above criticism. Suppose, for example, that pure and ap­plied science could not be neatly separated. Then pure scientists might be held socially responsible for harmful consequences of their scien­tific practice that might have been reasonably anticipated. Surely this would make scientists more cautious, and it could deflect the pure search for truth away from directions threatening lawsuits. In any event, argumentation would then transcend the realm of the pure investigation of fact, and begin to involve the notorious complexities and uncertainty of normative disputes. If the application of science helped to sustain a social system of disturbing inequalities and injus­tices, and even pure scientists played a role in the maintenance of this system, optimism concerning science would begin to run against some unpleasant realities. For philosophers, it may be tempting to argue that the unpleasant consequences of scientific knowledge are a measure of technological or political ignorance, and represent merely bad applications of a theoretically neutral pure knowledge. This has the consequence that philosophers can analyze logical structures within the domain of pure science without getting involved in controversial applications of science, and they can undertake this without grappling with the questions of social hegemony that inevitably play a major role in thinking about the value of societies in which big science cur­rently plays a major role. Without retreating into an antiscience or antitechnology irrationalism, a cynic might observe that a resolute terminological decision to defend pure science against applied science can quiet a wavering philosophical conscience over time. In this dis­cussion of science and technology, it will be suggested that the deci­sion to put a wedge between science and technology, no matter what its other merits, has precluded an understanding of the dynamics of modern science, since modern scientific progress depends at least partly on the technology required to produce the scientific instru­ments capable of wresting data from reality, and is inconceivable apart from that technology.

At first glance, a fairly sharp distinction between science and tech­nology can be made out. Before modern science, there were many technological discoveries that obviously could not have been depend­ent on prior scientific knowledge. Inventions like the spinning wheel, the loom, and even the steam engine did not depend on concepts derived from theoretical physics. Various problems and needs were solved, largely by visual comprehension and craft refinement, but also by a steady process of tinkering with slight improvements. The tech­nological discovery is typically a physical object or thing, or the dis­covery of a process for producing such a thing, rights to the produc­tion and distribution of which can be owned by specific inventors through such devices as patent rights. By contrast, scientific achieve­ments are not owned by persons, although persons get credit for mak­ing them; rather they become part of the intellectual resources of the entire scientific community through publication and other means of disseminating knowledge.⁷ Typically, as we have seen, the scientist puts special questions to reality that are designed to permit clear, recognizable, and repeatable answers. The questions for technology seem to come from more mundane problems and needs. How can this be done more quickly, more effectively, or more cheaply? These are the questions for technology. Technological questions can usually be phrased in existing language, and they may be put to technologists in a modern society by employers of some kind who wish specific problems solved. It is clear that scientific knowledge will be used by contemporary technologists to solve such problems, so that modern technology does not develop independently of scientific knowledge, as technology did in earlier times. Nevertheless, it seems impossible to extend these initial observations into anything like a satisfactory general distinction between science and technology, because the two seem inevitably to overlap in the careers of various inventors. From an earlier era, Leonardo da Vinci provides an interesting example, but perhaps Thomas Edison will be a more accessible figure for mak­ing this point.

Edison’s own self-image wavered considerably. By 1880, Edison thought of himself as a man of science whose achievements, such as the development of the first long-lasting electric light bulb, should be acknowledged on the standard scientific criterion of first publication.⁸ In the same year, Edison began to publish a journal called Science, the predecessor of the familiar current scientific journal. Although Edison made some purely scientific discoveries and at one time thought that he had discovered a new force, which he called etheric force, his fame rests on various inventions, of which his lighting system is a well-known example. Even in Edison’s time, it was not at all clear whether his proposed lighting system was science or nonscience (technology). Edison was invited to scientific meetings to read papers on the scientific aspects of his work, including the lighting system. At times, Edison preferred to keep various test results private, thus vi­olating the norms of exchange of scientific knowledge and evincing the behavior of an inventor, rather than that of a pure scientist. Ac­ceptance of Edison as a scientist enraged at least one prominent American physicist, Rowland, who clearly had Edison in mind in the following excerpt from an address to the 1883 meeting of the Ameri­can Association for the Advancement of Science:

The proper course of one in my position is to consider what must be done to create a science of physics in this country, rather than to call telegraphs, electric lights, and such conveniences, by the name of science. I do not wish to underrate the value of all these things; the progress of the world depends on them, and he is to be honored who cultivates them successfully. So also the cook who invents a new and palatable dish for the table benefits the world to a certain degree; yet we do not dignify him by the name of a chemist. And yet it is not an uncommon thing, especially in American newspapers, to have the applications of science con­founded with pure science; and some obscure American who steals the ideas of some great mind of the past, and enriches himself by the application of the same to domestic uses, is often lauded above the great originator of the idea, who might have worked out hundreds of such applications, had his mind possessed the necessary element of vulgarity.⁹

The passage is sufficient to indicate that scientists, as well as philos­ophers, have felt compelled to defend pure science against vulgar and self-serving applications.

Whatever the value of the idea of pure science to the motivation of scientists who are engaged in fundamental research, it is still clear that the payoff from science for society comes through applications that help to master nature, and the payoff from science for those who employ scientists is this mastery, plus, in many cases, related meth­ods of social control. It is clearly utopian to imagine that at this point a diminution in technological achievement might make our lives bet­ter. Technological inventiveness might be applied to problems of wider social significance, and the benefits of technological achievement might be more widely shared, but human life would undergo drastic changes for the worse if technological levels of achievement were to lessen suddenly. This can be seen clearly in the case of food production. Modern farming machines, fertilizers, and new hybrid species have combined to provide the possibility of feeding large populations through the work of a few.¹⁰ Land and labor productivity have soared during this period, and in the United States this achievement has been reached through highly successful agricultural research. This research effort is interesting in that the scientists involved have been located near the farmers whom they were to help, and this decentralization seems to have had positive results. The scientists involved were able to become familiar with the problems of local farmers, and local farmers found technical advice easily obtainable. In this program, scientific research was not separated from technical demands and was not pure, in the sense that much of it was related from its inception to potential farm­ing problems. Productivity in the American food industry is quite clearly related to the highly successful USDA research programs, and would be inconceivable without these programs. Separation of re­search and related technology may often be desirable to free research from any control other than the attraction to lines of research prom­ising epistemological advance, but it is clear that science must ulti­mately be coupled to technological applications if it is to be supported within a social structure. Just how this coupling can be best effected, and how research and development funds may best be spent, is a topic not within the major interests of this work, although it is widely pursued by economists under the rubric of science policy.

The picture of agricultural technology suggests that one difficulty in the problem of separating science and technology is that the prob­lem is considered primarily in the context of a society in which the roles of pure scientist and applied scientist have reached vocational separation. Intellectual discoveries in the domain of pure science are attributed to a discoverer, or a group of discoverers, but the results become ideally accessible to everyone through publication in learned journals. Practical discoveries are protected by patent rights and a legal system protecting the economic advantages of these rights. It can’t be concluded that the features of this system prove that a sharp distinction between pure and applied science exists in general. In the case of Edison the line is obviously blurred. Modern research in war­fare leads to pure and applied discoveries, but the distinction is once again blurred because all of the information is treated as a military secret and the normal device of publishing or seeking a patent does not apply.

So far, attempts to consider the relationships of pure to applied science have suggested that no sharp line of demarcation is possible. For our purposes, however, whether science and technology can be made conceptually distinct is somewhat secondary to the fact that modern science contains a major technological component in its in- strumentarium. Modern science is inconceivable without accurate pictorial representation and without the highly specialized scientific instruments that scientists use to investigate nature. This fact makes the question of the independence of science and technology moot, even though those concerned to defend pure science have frequently not noticed this important fact. It would be possible to write the his­tory of science in terms of the instruments that have been available for scientific use. From this standpoint, it is not surprising that math­ematics, astronomy, mechanics, and optics were among the scientific disciplines first to develop, since the data domains over which these disciplines theorize do not require complicated scientific instruments for their development. Of course, it is true that larger telescopes, and radio telescopes, for example, have extended astronomical knowl­edge, but the basic outlines of astronomy were set down with the aid of naked eye observation and the primitive light telescope.¹¹ Chem­istry, requiring complicated and specialized instruments, developed later. It would be wrong to suppose that chemists might have discov­ered the structure of complicated molecules before the development of sophisticated equipment whose data could guide such discoveries.

In addition to the instrumentarium, philosophers have overlooked the importance of technological developments in the visual presenta­tion of both instrumental design and factual material. Manufacture of scientific instruments would not be possible without exploded views of assembly, which manage to compress a great deal of information about their construction into an easily absorbed schematic form.¹² Vis­ual thinking and visual metaphors have undoubtedly influenced sci­entific theorizing and even the notation of scientific fact, a point likely to be lost on philosophers who regard the products of science as a body of statements, even if the statements have been guided by an intuition into the nature of things.¹³ Could modern scientific work be at its current peak of development without visual presentations and reproductions of photographs, X-rays, chromatographs, and so forth? To consider a more specific example or two, would astronomy be possible at modern levels without time-lapse photography, or physics without bubble-chamber photographs? The answer seems clearly in the negative. Even if the data gathered by many instruments could be expressed in statement form, it seems that in numerous cases a coherent grasp of data requires technological achievements that weld technology and science into an inseparable unity as a means of ob­taining knowledge about reality.

How is scientific knowledge related to other kinds of knowledge recognized in modern societies possessing a scientific component? Many philosophers have been tempted to drive a wedge between science and society, or at least to emphasize the independence of scientific knowledge from other forms of human knowledge. As with the rela­tionship of science to technology, their purpose in doing this is to avoid the recurrent problems of relativism and bias that seem to threaten if scientific knowledge is at all tainted by nonscientific knowledge and nonscientific interests. Science is seen by these philosophers as de­termining its own ends and pursuing them with its own logic. If this separation were possible, then an internal history of science would be completely satisfactory. An internal history of science seeks to explain the history of science solely in terms of goals set by scientists to solve purely scientific problems, and procedures (usually cognitive) deter­mined by scientists to maximize the changes of attaining such goals. Methodologists may seek to write internal history by giving a version of methodology, and then showing that some important segment of scientific history can be explained solely according to this methodo­logical conception except for lapses and errors in the judgment of individual scientists that might have been avoided if the methodology had been followed more rigorously. Actually, this has been done for segments of scientific history, particularly for the conceptions of methodology attributed to Popper, Kuhn, and Lakatos.¹⁴ Curiously, the same segments of scientific history can be made to fit any of these methodological schemes, showing that the slack between normative methodology and the details of history can be adjusted to fit various prejudices.¹⁵ An external history of science would argue that the course of scientific history can only be explained by referring to opinions, events, and needs, that are not purely scientific and are rarely men­tioned in the archives of scientific research, and it would argue that such material must be used in explaining the course of scientific history.

At first glance, the argument between those who feel that internal history will suffice for explaining the course of scientific history and those who feel that it will not seems inconclusive. Scientists are hu­man beings who do live in a society and have human problems, and it would be absurd to suppose that they could ignore their background completely when they were doing science. Only the fear that this must distort scientific investigation and adulterate it with subjective elements could motivate the desire to deny the legitimacy of the claims of external history. At the same time, it is surprising how far internal history can go in providing a convincing account of the details of sci­entific history. The only way to reconcile these two observations is to take the position that science is relatively autonomous from its social setting, that is, that scientific development requires less recourse to external historical factors than the development of other social insti­tutions. Nonetheless, a caution based on the sweep of scientific his­tory is in order. From the seventeenth to the nineteenth centuries, science was pursued primarily by individuals who were free to choose lines of research on the basis of personal preference, and whose re­search could be funded from personal income or by a patron. For this sweep of two hundred years, the internal history of scientific devel­opment is nearly the whole story. But in the last century, science has become much less independent of its surrounding society. Scientific research involves costs that in turn require the acceptance or coercion of large populations in sharing these costs. Individual scientists have given way to corporate or governmental financing. The relative auton­omy of scientific research from the society in which it takes place is therefore perforce weakening, and this raises a variety of questions that cannot be easily circumvented.¹⁶ Perhaps the most important of these questions is whether science as the successful pursuit of pure knowledge can maintain a high rate of progress if its autonomy is considerably diminished.

Now let us look a little more carefully at some of the relevant his­torical points. For an internal historian of science, the inescapable impact of surrounding nonscientific values and suppositions may only hinder the development of science. A scientist may be unable to think immediately of the solution to some scientific problem because back­ground presuppositions prevent formulation of a correct scientific an­swer. An internal history of the logic of the development can be writ­ten in which this event seems to show that actual scientific history is only delayed by scientifically irrelevant factors. In this way, the actual lack of autonomy in the real history may give rise to preference for an idealized internal history along with hopes that explicit methodol­ogy can help idealized behavior to occur more frequently. A useful example to reflect on in this connection is Kepler’s introduction of the elliptical paths of the planets around the sun in his picture of the solar system. Kepler began in 1600 with the usual view that the paths of the planets were circular, a view that had to be abandoned because of the accumulating data to the contrary. Kepler did not turn to the ellipse as the natural generalization of the circle, as we would. In standard analytic geometry, a circle is a special case of an ellipse, and this is perhaps why the ellipse seems the next most complex closed curve in space after the circle to many people. Kepler turned to the ovoid instead. The ovoid plays almost no role in modern mathematics, is difficult to handle mathematically, and has almost no instances in physics. But the ovoid does have one important property in common with the circle, a property it does not have in common with the el­lipse, and that is that it has only one focus. In a theological setting, where people were trying to describe God’s creation, this is impor­tant. According to the principle of sufficient reason, God always acts rationally, that is, acts on the basis of some persuasive line of argu­ment. If the planetary orbits are circles or ovoids, the plan of creation is rational, since a distinguished place is obvious for the sun at the focus of the orbits. If the planetary orbits are ellipses, the sun seems to be placed arbitrarily at one of the foci.

At a later time, when the connection between the inverse square law of gravitation and the elliptical orbits could be made mathemati­cally clear, the background influence of theology could be squarely confronted and laid to one side. When Kepler was working, the im­pact of theological background information made the move to the ovoid seem necessary, and alternatives could not be easily formulated and evaluated. Kepler came to the ellipse as a mathematical aid in calcu­lating ovoid orbits, and it was some time before he realized that the data actually fit the elliptical orbit better than the ovoid that he was trying to locate. Hanson cites this as an example of a necessary gestalt organization in scientific thinking that distinguishes great scientists from mediocre scientists.¹⁷ Perhaps this is better taken as an example of how background knowledge can coerce even pure theoretical spec­ulation in science.

At this point the methodologist is ready to argue that logic might have solved this quite nicely. Had Kepler formulated the logical al­ternatives, he might quickly have seen that the hypothesis of elliptical orbits was superior to that of ovoid orbits. The trouble with logic is that there are too many alternatives in logic, and that even the for­mulation of logical alternatives is dependent on the vocabulary avail­able to the working scientist or logician at a specific time.¹⁸ Scientists, as we have seen, rely on an intuition about what is relevant. In doing so, they will make mistakes, but they will keep alternatives to a rea­sonable and discussable few. If science is subject to background con­straints, how are these constraints to be transcended? The answer seems to be that they cannot be transcended by mere logic, since logic will frequently produce an unmanageable catchall hypothesis as one alternative in order to provide a full set of alternative hypotheses, and logical intuition will usually not suggest the interesting alternative within this catchall hypothesis that is needed for scientific progress. Put another way, logic can enable us to formulate alternatives that have already occurred to us, but it doesn’t produce new hypotheses.

We have already observed that pure science, perhaps because of a desire to differentiate itself from applied science, has frequently ar­gued that its pursuits are disinterested and motivated only by pure epistemological considerations. Scientists themselves have attacked one another with the charge that research may be motivated in some cases by social interests, a charge that compels an attempt at rebuttal, given the social norms of scientific controversy. In the recent IQ debates, those supporting genetically based IQ differences between various groups of human beings have been challenged with the claim that their science is not pure, but is motivated out of racial prejudice and is designed to implement biased social programs.¹⁹ Even though purely theoretical rebuttal of the methodology of much of this work seems sufficient to indicate that the inferences it makes from data are mis-

taken, the theoretical rebuttals have often been accompanied by nasty ad hominem remarks about the purpose of the research. Pure scien­tists like to consider their research independent of social motivation or social demands, lest their research slide into applied or technolog­ical categories. If research is applied or technological, it seems to take sides and to look toward a predetermined end. It is, in short, no longer free to pursue the pure logic of inquiry. But there is the fol­lowing problem confronting any able scientist, namely, that a vast welter of possible lines of research stretches out from the present point of accomplishment. Which of these lines should be chosen to guide immediate research? A scientist may choose to work on a line of research that he or she feels may lead to personal success and acknowledgment of that success by other scientists, rather than on that line of research which seems to offer the greatest possible bene­fits for mankind. (It can be assumed that these lines will sometimes diverge.) This choice is personal and subjective, but it is not usually recognized as such, since it is concealed in the passive prose of sci­entific papers that cite a direction of research without indicating why quite different lines of research were not pursued. Again, a scientist might pursue a line of research out of some social commitment. The mere fact that a topic is chosen one way or another does not preclude that good science may result from its investigation. There is no ne­cessity for a scientist who has chosen a goal to cheat or even lower his or her scientific standards, whether that goal be motivated partly from personal factors or from some social commitment.

An example that may serve to illustrate this process without involv­ing contemporary controversy is the phrenology debate in Edinburgh between 1800 and 1830.²⁰ Phrenology stood opposed to the beliefs of the Scottish Enlightenment in proposing a nativist explanation for hu­man behavior, and in seeking educational systems, penal systems, mental institutions, and even factories that might modify the innate dispositions that it sought to uncover in human beings. These dispo­sitions were thought to be coded in specific areas of the brain. The phrenologists anticipated that the brain would be a complex organ whose specific parts served distinct mental functions. Abnormalities in the suborgans of the brain would lead to abnormalities of behavior. Neither the phrenologists nor the Scottish physicians and philoso­phers opposing them could directly correlate brain anatomy with skull shape or behavior, but the phrenologists supposed that the shape of the skull was caused by the underlying brain, and they attempted to correlate behavior and skull shape to establish their convictions, al­though anatomical dissection of brains was also involved. Although phrenology is no longer regarded as a science, the conviction of the phrenologists that the brain was a combination of specific organs was much closer to the modern view than the contrary conviction of their opponents. A huge dispute arose around the frontal sinuses. These sinuses could cause nonparallelism between the skull shape and un­derlying organs. The phrenologists minimized any nonparallelism and their opponents maximized it. As usual in such disputes, the two sides actually saw and drew slightly different sinuses, but current anatomy is not incompatible with the phrenologist’s drawings of the sinuses. Needless to say, the phrenologists were attacked by licensed physi­cians because of the contamination of their knowledge by social goals. The social goals of the phrenologists are undeniable, but so is the fact that their anatomical work was important for the advance of medicine. An interesting difference between the phrenologists and the physi­cians is that the phrenologists were outsiders, in many cases foreign to Edinburgh or not part of the scientific and intellectual elite of Edinburgh. The social interests of the scientific elite are also evident in their research, but not quite so vulnerable to attack because de­fending their institutional privileges could be carried out without wildly upsetting a social structure in which those privileges had their place. A great deal of science is done without overtly threatening surround­ing society, and histories of science tend to rely on the history of orthodox science, ignoring the social commitment of orthodox and unorthodox alike. But when we look at the details, we find that much of current science comes from historical controversies in which both sides had some sound scientific intuitions, and in which both sides made contributions to later scientific understanding. Perhaps it is clear then that good science can grow out of a quite interesting choice of a line of research, and that the attempt to deny that these interested choices play a role in science is nothing but a mystification designed to make science mysterious and incomprehensible to nonscientists and to support the notion that pure scientists are quite different from their fellow citizens.

It has just been suggested that a scientist may choose a line of research for many reasons other than its sheer epistemological poten­tial, and that this need not preclude good scientific work. On this model, however, the scientist is still conceived of as an individual making a personal choice of research topic. In the past, when science was pursued by individuals, science was pursued almost independ­ently of surrounding social chaos or coercion, since individuals were still free to make their own decisions. The twentieth-century inter­penetration of government, science, and technology threatens this picture, and may even threaten the existence of successful science. Internal histories must remain ignorant of this threat, since they dis­miss this interpretation and its associated funding complexity from the field of investigation. Popper has been alert to the problem, but he has argued that science is the model of a free and open society, and that it can function properly only when it is allowed autonomy and feedom.²¹ He sees science as a delicate cultivated flower of Western civilization, a flower that is likely to die if its conditions for existence are changed very much. The difficulty with Popper’s view is that sci­ence does not seem as free and open as it is on his normative char­acterization, and it is quite clear that science has flourished in other than free and open societies in Popper’s sense. Popper sees science as necessary to solve problems facing society, and is worried that it may not solve problems rapidly enough in a transmuted form. Ravetz has contributed a brilliant and incisive analysis of the state of contem­porary science, arguing that the system of criticism between compet­ing scientists that has maintained quality control over scientific work and supported the reward system so necessary for scientific motiva­tion (in this respect his framework is similar to Popper’s) is breaking down, and that science shows signs of degenerating in quality and becoming a social system in which the political trade-offs of other social systems are becoming depressingly operative.²² By contrast to Popper and Ravetz, Kuhn’s treatment of scientific history allows no place for such worries, and seems to assume quite blandly that a func­tioning scientific work force is a natural part of any modern society. It seems clear that we have reached a time when the interaction of science, government, big business, and technology precludes any simple notion that a purely internal history of science can explain the current direction of scientific research. The philosophy of science thus needs to broaden its scope in order to consider how a negotiated autonomy for science can best be brought about so as to avoid the obvious po­tential for corruption in government and business funding for scien­tific research.

Public funds can be spent in obvious ways on social programs that will clearly alleviate human misery. And, of course, it is possible to imagine fewer public funds being spent. When public funds are spent on scientific research, a huge gamble is taken, no matter how the funds are dispensed on the research. Money can be spent in an area where some scientific solution seems desirable—but the solution may not come. And money can be spent under conditions that mean sci­entists are free to pursue their own ends—nothing may be discov­ered, or something enormously valuable might be discovered. Sci­ence policy attempts to look for rational guidelines for spending such money, but the obvious risks make a rational policy difficult to imag­ine. The situation is not like betting in connection with uncertainty, where the range of alternative outcomes and their chances of occur­ring cannot be reasonably canvassed. Because of these difficulties, the two pure positions are either that government should support science as much as possible while maintaining no control over its direction (the classic stance of the defenders of autonomy), or that science should fund only those lines of scientific research that have reasonable ex­pectations of public benefit. Neither of these positions is ultimately defensible. The position of autonomy isn’t defensible because not all that research scientists would like to do can be funded by public money, and because research programs may conflict in their experimental de­sires, so that some principle of selection of programs for funding is requisite. The social good position isn’t defensible because it does threaten the health of science, and because reasonable expectation is so hard to assess. Compromise positions also have difficulties, as can be seen in connection with the finalization debate in Germany.

The finalization debate in Germany has its origins in an apparently innocuous extension of Kuhn’s theory about the history of science proposed by some members of the Starnberg Max Planck Institute.²³ According to the Starnberg group, Kuhn’s model of history is essen­tially correct, and scientific history can be written internally through the phase of normal science governed by paradigms. But it is possible for a discipline to reach a postparadigmatic stage in which theories are no longer tested and extended so much as applied. At this point, the orientation of theory development is no longer controlled by an internal logic, and the application of theory can be fixed by external goals. This position concedes that research planning isn’t possible when research is ‘pure,’ that is, devoted to novel topics and shifting in ac­cord with new discoveries. Revolutionary epochs and early paradig­matic stages of scientific disciplines thus elude rational control. But in the postparadigmatic stages of scientific disciplines, externally im­posed goals can affect even the internal logic of scientific develop­ment. This position is distinct from the position of autonomy, because it denies that internal logic always determines the course of pure sci­ence, and is distinct from any form of Marxism, which argues that needs external to science always determine the course of scientific development. As a result, the Starnberg thesis has been attacked from left and right, each side primarily arguing that, on its terms, the Starnberg thesis is wrong. The real problem is that the Starnberg thesis is dangerously vague, since no definition or characterization of postparadigmatic science is offered, and this leads to the threat of political chaos in any attempt to implement the Starnberg thesis. Ag­ricultural chemistry and chemical engineering can be given coherent external direction, but are these postparadigmatic sciences compara­ble to postparadigmatic physics or chemistry or biology? The obvious feeling that there is some difference between these groups of subjects in terms of cognitive goals highlights an example of the difficulties with the vagueness of the Starnberg notion of postparadigmatic sci­ence. Perhaps postparadigmatic sciences can be externally controlled toward socially chosen ends, but not all scientific disciplines at any given time are likely to be in this convenient stage. How are the non- postparadigmatic sciences to be funded when they require large public expenditures? We are back at square one, and the depressing suspicion intrudes that the important problems confronting science policy may have no rational solution.

As in the previous section, it has been argued here that there is no absolute wedge to be driven between science and technology, and none to be driven between science and society. Science and technol­ogy have become inextricably entangled, and scientists are human beings, which means that personal passion and bias will affect them as scientists and that pressure from surrounding society will inevitably influence their choice of relevant scientific work. The effort to drive these wedges is an effort to preserve the epistemological purity of genuine scientific practice. While all of this is true, the history of science can be written as an internal history far more successfully than the history of governments or religions. All that has been suggested so far is that the relative autonomy of science is not to be explained by the purity of motive of the individual scientist, or by alluding to a definition of pure science thought to be instanced in the best scientific practice. In order to advance beyond this point, some important as­pects of scientific history must be considered.

Science and Common Sense

We have already suggested against claims for the autonomy of science that the relative autonomy that could once be associated with the individual researcher is no longer tenable as a picture of basic scien­tific research in the age of big science. Science and technology, sci­ence and background social factors, even science and pseudoscience, are impossible to separate analytically in conformity with what is known about scientific history. At the same time, it was suggested that sci­ence is probably the most autonomous social institution among all the nonautonomous social institutions, and the one social institution for which internal history can come close to an explanatory account. It has been argued that the scientist cannot reason informally, nor make naked eye observations, any better than many nonscientists. The gen­eral cultural outlook of the scientist will also have an impact on his or her choice of scientific research. None of these observations engages the fact that the scientist’s scientific reasoning is aided or amplified by mathematical systems, that the scientist’s scientific observations are aided by scientific instruments, and that the scientist’s expression is constrained by a social system designed to criticize and discuss that expression as part of a competitive process with clear, even if some­what informal, rules of struggle. These features mean that the scien­tist is pulled along paths of discovery that may well be repugnant to common sense, even his or her common sense, but forced nonethe­less by the structure of scientific investigation. Although common sense itself will change over time, it is clear that at any given time, science and common sense can be in direct conflict. Moreover, this situation may be typical. Scientific knowledge seems frequently to involve a ‘break’ with common sense, and its apparent autonomy must be re­lated to this important fact. Let us look at this more closely.

First, the objects of scientific investigation are rarely, if ever, iden­tical with the objects of common-sense knowledge, even if the occur­rence of the same names in scientific discourse and everyday language suggests some relation of reference. One may note that one-time sta­ples of common-sense explanation, such as ‘fire’ or ‘air,’ often simply disappear in developed scientific discourse.²⁴ The facts about some particular fire or a particular body of air may be studied scientifically for some purpose, but ‘air’ or ‘fire,’ elements of an earlier cosmology, have no important place in contemporary science. Now let us consider common terms. The sun is an object of everyday comment and also of scientific investigation. It is clear that the properties of the sun as an object of informal observation and as a scientific object are quite distinct. Scientists consider the sun to be a point, or an enormous oblate spheroid, or whatever, depending on the scientific context in which it is being studied. Many philosophers have argued that the sun of everyday life is the same object as the sun of science. If the propositions about the sun in the two discourses have the same ref­erence but the discourses are contradictory, then to restore consis­tency one discourse has to be translated into the other, or both dis­courses have to be translated into some neutral discourse. Using the ontology suggested in the first chapter, we find it more appropriate to say that the sun is a complex object that reveals a certain side to everyday discourse and quite a different side to scientific discourse, but that neither of these discourses is neutral or primary. Both are directed to different ends and have different purposes. Thus there is only one sun, but there can be no full description of it in any neutral discourse, so we can’t say exactly and fully what one sun actually is. This does not preclude our being able to say fully and exactly what the sun is in some discourse for some particular purpose.

Historically, there was a time when scientists were studying the sun without thinking of it as distinct from the object of everyday dis­course. Later, the discourses of science and everyday language are distinct, if not incompatible. Some philosophers have been tempted to suppose that the meaning of scientific discourse is to be understood by tracing its roots to the meaning of everyday discourse. This seems to reconstruct a historical process. Scientists began speaking everyday language and talked their way into a scientific manner of expression. In many cases, such as sun and mass, the same word occurs in both discourses. But unless one holds the extremely dubious position that all languages are intertranslatable, it is clear that we can learn other languages by starting in one language, discussing features of the other language such as the general sentence structure, the meaning of par­ticular intertranslatable words, and wind up communicating in the new language, even though the two languages are not fully intertrans­latable. This simply means that some growth or change occurred that transcends translation. Participation in a new form of life or a new culture suddenly causes a new manner of expression to snap into place. Kuhn has pointed out that graduate education plays this role. The fledgling scientist, by doing science, comes to participate in a scien­tific conceptual framework and an associated language. This is why science can’t be exported through books, but needs to be exported through participation in scientific education, including laboratory practice.²⁵ Perhaps, then, entry to the meaning of a scientific dis­course is to be understood in one way by tracing its development from everyday discourse, but this does not mean that the meaning of the scientific discourse is reducible to, or translatable into, everyday dis­course.

The leap to a scientific notion has been brilliantly discussed by Bachelard.²⁶ One example he discusses extensively is the concept of mass, which on his analysis appears as five different concepts in its history. In its earliest, naive realist, form, mass is equivalent to sheer bulk. We desire the largest fruit, let us say, for our dessert. But the biggest of a kind is not necessarily the best. There may be hidden defects. From this observation of a possible delusion, a concept of mass as density was noted, and the scale came to operationalize this concept. Not the largest head of lettuce, but that weighing the most is what I should like for a fixed price. This concept of mass is positivist and operational. Both of these first two notions, perhaps separately learned in the history of many individuals, are prescientific. Newton represents the break to science when he sets force equal to mass times acceleration. Now mass is no longer a direct observable, but plays a dynamic role in a system of theoretical relationships. Special machines to measure forces and accelerations are developed by physicists, and mass is embodied in a special mathematical system that is separate from ordinary discourse, involving a special notation that one must learn to operate with. Mass is now relative to other features of an object, and becomes a quite complicated notion. Relativity again com­plicated the notion with the distinction between rest mass and mass in motion. In the mechanics of Dirac, a single object may have two masses, one of them negative. This total movement is marked most decisively by the break from mass measured by scales to the theoret­ical mass of Newton. At this point, there is a break that cannot be translated back into earlier discourse. That is why a scientist can learn classical mechanics, not by reconstructing history, but by learning the language of classical mechanics directly and then doing things with it, including the making of experimental checks on theoretical reasoning. According to Bachelard, the creative dreaming of the scientist occurs because of the layered concepts, like that of mass, which are the in­struments of speculation rather than the instruments of experimental check. The internal structure of scientific concepts, quite contrary to the desired conceptual simplicity of much philosophizing about sci­ence, is a valuable component in fueling scientific progress. What is common to various scientists is the existence of the various subcon­cepts of a concept like mass, although the emphasis or profile of im­portance of these subconcepts will vary from one scientist to another. A particularly valuable exposition or discovery by a scientist will ap­pear in a discourse flattened out to the consistent expression of only one concept, but the significance of the work will depend on the linkage and resulting suggestiveness of the subconcepts. This Bache- lardian view helps to capture the complexity of scientific autonomy. Discourse can be autonomous, but it tends to be influenced where it is speculative by the archaeological structure of concepts.

There is usually no question that physics is a paradigm natural sci­ence. The development of a concept like that of mass consists in grad­ually ‘bracketing’ away layers of presupposition that are involved in everyday discourse. The more recent and most advanced physics, conceded everywhere to offer the deepest insights into reality, is the most self-contained and least dependent on everyday notions. Physics has evolved steadily away from everyday experience and everyday discourse. This is not surprising in the least. Everyday discourse is self-satisfied. At the everyday level, we can explain everything, per­haps by recourse to divinity or to classification of something as bi­zarre, but nonetheless we are pretty self-reliant in our mother tongue when confronted with the problems of daily life. Dissatisfaction with the obvious and suspicion of the easy answer underlie the drive of scientific thought. This is shown in a most engaging way by Ronchi in his history of optics.²⁷ At one time, areas of physics incorporating human perception were thought of as legitimate branches of science, for example, acoustics and optics. They remain, but their luster is considerably diminished. As Ronchi shows in connection with the the­ory of optics based on mathematical geometry, the human observer looking at images formed by mirrors with various kinds of surfaces will frequently see images other than where the theory predicts. For example, a human will frequently see an image on a mirror surface when theory places the image in front of or behind it. Human per­ception is constrained in various ways not anticipated by the theory because of knowledge of the probable size of such objects as human beings and candles. Optical experiments therefore do not necessarily reveal reality as opposed to human perception of reality, and optics is not really pure physics. This insight is related to Bachelard’s dictum that reality comes at the end of science, and not at the level of every­day discourse. We begin with our internalized cultural reactions to the world. After an epistemological break to science, we may attain a description of reality itself, at least of one stable and calculable aspect of reality.

To this point, a semantic shift in the reference of terms along with the introduction of new terms has been cited as involved in the epis­temological break to science. It is also true that syntactic differences between scientific discourse and everyday discourse can be noted.²⁸ For example, the use of past and present tense may not mark a tem­poral distinction in the ordinary sense, but indicate whether or not apparatus being described is thought of as temporary or permanent. “A cyclotron consists of... ” is different in this respect from “A glass tube was inserted into the apparatus at point A.” The past tense is appropriate for describing apparatus set up only to function in a par­ticular experiment. A second example is the peculiar use of given in scientific discourse. Consider this example: Figure 9.5 shows how the vapor pressure of a given substance changes with the temperature.

The use of a or any instead of given in this sentence changes its meaning. Given functions here to mark out a definite substance ar­bitrarily chosen from a range of implied alternatives, a task seemingly frequently required in technical and scientific writing.

Unfortunately, there seems to be nothing in the semantic and syn­tactic shifts required by scientific discourse to indicate what is dis­tinctive about scientific epistemology. Almost any move to highly spe­cialized interests will be accompanied by semantic and syntactic shifts, although specialized interests need hardly be scientific. Sports writ­ing, movie reviews, astrology columns, horse breeder’s manuals, cookbooks, and so on, may all be written in a distinctive style that involves reference to features of the world not coded into everday discourse. All of these areas may involve an epistemological break with common sense, and it may not be possible to translate all of the relevant assertions back into everyday discourse. Everyday discourse may not contain the resources to define concepts that are related to specialized and invariable experience, so that words for these con­cepts involving extended and discriminate perception are best spe­cially coined for communication among experts who are familiar with their specialized problems. Once a few of these terms have been de­veloped, the language of specialty then has a life of its own. Perhaps lengthy and circuitous paraphrase can suggest the meaning of terms in the language of specialty, but there is no substitute in their mastery for the appropriate experience.

Specialized languages for specialized purposes may be relatively autonomous from the languages from which they were derived. Per­haps English and German, or some other pair of everyday languages, are not intertranslatable. What this may mean is that the languages are associated with quite different forms of life or cultural settings, so that the typical speaker of one language may use a word to describe an experience in a kind of setting that is not at all common for speak­ers of the other language. A word may thus exist in the first language and have no real equivalent in the second language. Could a word be added to the second language? Yes, but the point of so doing, or the success in so doing, remains obscure if the relevant experience is missing. The languages as used in religion or law may not be trans­latable because the relevant experiences in the two cultures in these areas are diverse. But specialized interests mean a focus of concentra­tion. Two horse breeders, boxers, coaches, cooks, or whatever from two cultures may discover that they can communicate fully adequately just in the area of their common interests. Scientific discourse in var­ious languages has not encountered the sorts of difficulties in trans­lation notorious in the translation of poetry just because of the spe­cialized interests and concerns of the scientists. It is not that scientific discourse is primarily declarative and that assertions can be more readily translated than metaphors, as it is sometimes supposed. It is rather that science concentrates on specialized problems and utilizes expe­riences that are not culture specific in the usual sense. Science, how­ever, is a secondary culture, like many other specialized interests, and it filters out unique cultural experience because of shared activi­ties, and can hence be produced as a (relatively) autonomous subcul­ture in a very similar form in a variety of primary cultural settings.

To this point we have been operating almost entirely with an epis­temological and sociological set of tools. While repudiating traditional forms of epistemology for their failure to deal adequately with scien­tific knowledge, and repudiating the claims of sociological inquiry to locate the distinctive features of scientific knowledge, we have only been able to offer a vaguely characterized dialectical conception as an alternative to these traditions. That science is reached by an accultu­ration process into scientific culture involving an epistemological break with common sense seems to be true, but it once again fails to distin­guish science from acculturation into other specialized interests. From this point on, we will set the critique of existing programs into the background, and turn to the development of a more positive charac­terization of our dialectical conception of scientific growth. The first element we require can be obtained from an examination of the con­cept of scientific history that underlies both the epistemological stance so common in philosophy and the sociological stance involved in sta­tistical investigation.

Science and History

When we look back at the history of science from the viewpoint of the present, it is often possible to discern which were the important moments contributing to the history of science, and which were merely dead-end speculations. The former moments are simply those that have had consequences that led to the present. The latter have no important consequences in the present. Any supposition that there is a methodological characterization that can separate progressive from nonprogressive moments in scientific history ignores a basic fact about the temporal perspective from which we must view a historical mo­ment. Viewed retrospectively, a moment has a significance dependent on what has happened between that moment and the present. A con­temporaneous moment cannot yet have this significance. Unless the future significance of what occurs at some moment can be determined at that moment, it is quite possible that it is impossible to tell at a moment in time which are the important scientific achievements; this can be known only retrospectively. Thus our knowledge of scientific history may not help us to fully evaluate contemporary science or to project the future significance of contemporary science. In this sec­tion, the relationship between history of science and the philosophy of science will be explored. Philosophy of science has typically as­sumed that a rather naive narrative account of scientific history is not only possible but the only possibility. When a more subtle account of scientific history is introduced, it should become clear why the dia­lectical attitude is necessary to understanding science. It should also become clear why neither scientific fact nor scientific theory can be set down as having fixed significance. That scientific fact cannot be set down in this way is important in transcending empiricism, but its importance is not evident until a better historical conception is at hand. The dialectical development of theory and experiment is inter­nally related to the difficulty of evaluation of the present moment in science, a difficulty that may be maximized in some sense in scientific progress.

The most subtle barrier to the conception of history to be argued for is perhaps the failure to realize that any narrative account of sci­entific history, undertaken as it must be from some point in time, will utilize the scientific vocabulary of that time in order to attempt de­scription of the past. Unfortunately, neutral description of the past in terms of contemporary vocabulary is not possible. Current scientific vocabulary is that vocabulary which has turned out to have high utility for current scientific description. This vocabulary contains within it an evaluative component that reveals what is now considered to be good science. If the scientific past is described in present vocabulary, we can tell from the description what is good science, that is, what has led to the present. Any attempt to circumvent this is to reintro­duce the confusions of the past into the account. To make it clear what is being argued here, two chemistry experiments from the his­tory of chemistry will be considered. At first, these experiments will be described from the viewpoint of their own time. What was a brown stuff of indeterminate nature will not at first be given its modern name, but simply be regarded as brown stuff. This is how we shall try to stay within the correct time framework. Both of these experi­ments seem to fit any reasonable description of sound experimental technique when viewed from the perspective of their own time. When these experiments are redescribed from the standpoint of the present, it will become clear which of them was progressive and which was not. The modern description locates the source of error in the one experiment, since now that we know what a chemical element is and which substances are chemical elements, the one experiment has to be seen as attempting to prove an element to be a compound (in modern terms), and hence is hopelessly wrong from our point of view. This historical exercise may prove sufficient to point to the unnoticed innocence involved in any idea that we can provide a simple narrative description of the past.

The two experiments to be described are chemical experiments, and they were performed during a period in chemistry in which there was intense investigation by chemists of what substances were chem­ical elements and what substances were chemical compounds.²⁹ These experiments were part of a sequence of such experiments, and the two chemists who performed them were aware of one another’s work, and were in effect criticizing one another by performing these exper­iments. One chemist sought to prove that one of the substances in his experiment, which we will call X, was a compound composed of chemical element Y and another substance, and the other chemist sought to prove the chemical opposite with his experiment, namely, that Y was a chemical compound composed of chemical element X and another substance. The two experiments are therefore chemically contradictory, and one of them must be wrong, given the structure of modern chemistry. If the experiments are described in modern vo­cabulary, the wrong experiment will be obvious, since we now know which are the chemical elements and which are the compounds. At the time when the experiments were performed, there was no uni­form chemical vocabulary (the substances used had names like calx and minium), and the two chemists had to exchange materials in a sequence of experiments to make sure that the X and Y they were using were in fact the same substances, so that their experiments were in actual conflict.

Now let us describe the two experiments in fairly abstract terms. The first experiment is designed to show that X is a compound by making it from Y and Z, through the application of heat. The second experiment is designed to show that Y is a compound by making it from X and U, through the application of heat. At a very abstract level, the designs are nearly identical. In the first experiment, liquid Y is placed in a retort connected to a quantity of gas Z collected over water in an inverted glass container. When the retort is heated, a solid X appears on the surface of Y and a quantity of the gas Z over the water clearly disappears. This experiment seems to make X from Y and Z, apparently establishing that X is a compound and Y is an element. In the second experiment, a quantity of X is placed on a wooden boat on the surface of water over which the gas U has been collected in an inverted glass container. An application of heat brought about by concentrating the sun’s rays on X with a magnifying lens suddenly causes the water to rise in the inverted container, X and U to disappear, and a quantity of Y to appear on the boat now at the top of the inverted container. This experiment seems to make Y from X and U, apparently establishing the proposition that Y is a compound and X is an element, a proposition that cannot be chemically recon­ciled with that established by the first experiment. It might be noted that both chemists accepted (correctly) the idea that the glass, water, wood, and methods of heating were chemically irrelevant to the out­comes of the experiments.

Both of the experiments described seem methodologically sound. Indeed they are virtually similar in design, since heat is used to create a new substance from two existing substances. The difference be­tween them lies entirely in the fact that an erroneous chemical con­clusion was drawn from one experiment. When the experiments are redescribed by identifying Y as mercury, X as mercuric oxide, Z as oxygen, and U as hydrogen, the apparent conflict is easily resolved. Actually, the gas in the container in the first experiment was ordinary air, and the oxygen is removed from the air in the experiment, but this does not affect the chemistry. The first experiment makes mer­curic oxide from mercury and oxygen, and the second experiment makes mercury from mercuric oxide and hydrogen, and now one sees immediately what went wrong in the second experiment. Mercuric oxide and hydrogen and heat make mercury and water, a fact that becomes obvious when balanced equations corresponding to the ex­periments are written out. Lavoisier performed the first experiment, and Priestley the second. At this point there is a methodological temptation to suppose that close observation might have detected the water produced in the second experiment, so that it could have been seen at the time to have been in error. In fact the possibility of water production in the second experiment was discussed by the two men, and the experiments were redone with the gases contained over mer­cury, rather than over water. Some water was noticed in the second experiment. Priestley attributed this to water impurity in the mer­curic oxide or the hydrogen that he was using. This guess, while at least partly wrong, was perfectly reasonable and couldn’t have been ruled out as wrong at that time. The manufacture of chemicals was not exact enough, nor were balances exact enough, to distinguish the error in the second experiment. In our time, the availability of better chemicals and better instruments, plus the conservation principles and the widely verified system of chemistry that has grown out of Lavoisier’s work, enables one to show the error in the second exper­iment. At the time, the experiments were the crux of controversy that was quite explicit, but not resolvable in terms of the techniques avail­able then. This is a good illustration of a point made earlier, namely, that science at any time is partly dependent on the available technol­ogy for producing experimental equipment. The overriding point is that our temporal perspectives give these two experiments a com­pletely different comparative significance that would be lost in any simple methodological discussion from a contemporary perspective.

Priestley was a supporter of the phlogiston theory, which has been roundly criticized as methodologically faulty by many philosophers and historians of chemistry. There is a persistent tendency to argue that the phlogiston theory was logically inconsistent, entailing such notions as that of negative weight.³⁰ Consider once again the equation from the second experiment stating that mercury is produced from mercuric oxide and hydrogen (phlogiston), and try to view it from an eighteenth-century perspective. It was discovered that when a metal was burned, the resulting oxide was heavier than the metal that had been burned. This suggests that the hydrogen driven out in the burn­ing has “negative weight,’’ that is, less than no weight at all—thus causing an indirect suspicion that some factor is missing in the account of the second experiment. Phlogiston theorists took this factor to be water, and argued that burning could only take place where free water was available to replace the phlogiston in the reaction. Their obser­vation was that there always was plenty of free water around in the crucial experiments. This is to recognize the importance of water in the reaction, but it places the water on the wrong side of the equa­tion. Only a better analytical chemistry and later experiments could show this supposition to be wrong, but the pressure to make the supposition shows that the phlogiston theorists were as anxious as their opponents to avoid discovered logical inconsistency.

When we look at the history of science, it may seem that observa­tion was precise and that the progressive can be sharply distinguished from nonprogressive. The example of the Lavoisier-Priestley confron­tation, in combination with many other similar examples that could be produced, should be sufficient to indicate that this is frequently a result of relabeling the past with the labels of the present. Philoso­phers of science have tended to be too naive about history, supposing that the security of the present would suffice for neutral description of the past by an appropriate methodological shift.³¹ A scientific dis­covery, like many historical events of importance, makes a number of later events possible, events that could not occur without it. When one of these possibilities is actualized, it gives the discovery a signif­icance it could not have had before this actualization. There is a sense in which we can only understand a discovery after its potential con­sequences are realized. The process in science of attributing discov­eries to individuals is the way in which this process is acknowledged.

What is being said here applies equally to the level of scientific fact and of scientific theory. The significance of both is determined typi­cally over time after an initial proposal. Should science be considered a matter of fact and theory, it must also be considered a matter of significant fact and significant theory. A fact, to become incorporated, must be of the sort that gives some theory significance, and a theory, to become incorporated, must be of the sort that gives at least some facts significance. Theory unassimilated to fact and fact unassimilated to theory will eventually drop out of science after a trial period. At any given time, there will be assimilated fact and theory in science, but also newly proposed facts and theories. Their significance and their longevity will depend on the development of a tissue of connec­tions to existing fact and theory as well as fact and theory yet to be proposed. Mindless accumulation of data is, in the long run, irrele­vant. That is why totally accurate observation of some succession of events at some arbitrarily chosen point is unlikely to be of scientific value, and is also unlikely to remain part of the scientific corpus. It is unlikely to call for a theoretical explanation sure to be of value in predicting the course of events elsewhere. We can summarize this line of thought by saying that science is interested in significant facts and significant theories, that is, facts and theories of mutual rele­vance, and not in the accumulation of mere theory or mere fact.

That a fact requires a theory to be significant, and to be retained, is shown by our chemical example. The two experiments were de­signed partly to show opposite facts: one the fact that X is a com­pound, and the other that X is an element. When the experiments were first performed, there was ipso facto evidence for both of these contradictory assertions. Both experiments and their results were part of the factual basis of developing chemistry. But what the experiments showed wasn’t settled until a chemical theory was developed that could explain the results of both (and many other experiments) satisfactorily, while a rival theory showing the experiments to have an opposite significance couldn’t be developed over the same range of data. Then it became a fact that one experiment was taken to have a fixed signif­icance, and the other experiment was reinterpreted. After this, both experiments dropped out as insignificant. They no longer had any­thing to say to chemists. Their significance was exhausted. What they had to say became part of the vocabulary of chemistry, and the focus of chemistry was on new topics.

Another example may not prove superfluous. A frequently cited example is Mendel’s work on inheritance, published in 1866 but not really influential until 1900.³² Was Mendel so far ahead of his time that his discovery was too revolutionary for his contemporaries to grasp? Or is it the case rather that Mendel’s work was of no particular sig­nificance until Darwin’s theory of evolution had run into difficulties? To begin with, it should be explicitly noted that Darwin’s theory was not published (1868) until after Mendel had completed his work. Fur­ther, Darwin’s theory, while explaining evolutionary change over time, did not contain a description of a satisfactory mechanism for explain­ing the rate of such change, or the fact that some characteristics of organism did not disappear, but might suddenly reemerge. Darwin’s own hypothesis of pangenesis was inadequate to this task. Mendel’s rediscoverers (De Vries, among others) were searching for a mecha­nism of inheritance that could support Darwin’s theory and replace the hypothesis of pangenesis. What they found in Mendel was deci­sive evidence for discontinuous evolution, evidence leading eventu­ally to the theory of the gene. Mendel’s observation of ratios now took on a significance that Mendel himself seems not to have been aware of at the time of his experimentation, and could not have been aware of unless he had anticipated Darwin’s theory and its difficulties. What we now encounter as Mendel’s experiments, with their associated sig­nificance for evolutionary theory and the mechanism of inheritance, is a historical reconstruction to be dated at least thirty years after Mendel’s own publication. From our current point of view, Mendel observed a fact, but the fact that Mendel discovered did not become significant until 1900. At that point, it became a significant fact be­cause of its relationship to evolutionary theory, and it has since re­mained an essential element of the factual basis for biological theory.

Just as the significance of fact may be revealed by the appearance of theory, the significance of theory may be revealed by the appear­ance of fact. Non-Euclidean geometry and noncommutative algebra, as is well known, provided a way of interpreting facts in newly emer­gent areas of relativity theory and quantum theory. In the crudest cases, a sufficiently bad theory may be recognized as having no sig­nificance by sufficiently recognized fact, and a theory may be recog­nized to have greater significance than before when it permits the deduction of a fact that is then confirmed by experiment. Between these cases, the range of significance of theory may be widened or lessened by discovery of its ability to integrate apparently unrelated facts, or by the discovery of facts seemingly closely related to the facts that it can explain for which no existent alternative explanation seems available. This part of the dialectical interaction needs no particular historical examples, since the evaluation of prior theory by newly dis­covered fact has played an important role in empiricist philosophy of science. It is, of course, being argued here that neither theory nor fact has precedence, and that the significance of both is under con­stant scrutiny in any healthy science.

In the Appendix we will confront some problems associated with differences in the development of the natural sciences and the social sciences that will mean that the account given here is primarily de­scriptive of the natural sciences. For the natural sciences, the devel­opment of experimentation does not involve the difficulties confront­ing social experimentation. But in both cases, it will remain true that the past of a science exists in its present, in that what has proved most significant and valuable has been assimilated into the current language and instrumentation of science. The present, however, does not contain sufficient information for us to grasp fully its significance. This view seems true of human history in general and of scientific history in particular. Once it is granted, it is no longer possible to retain the idea that a fully comprehensive methodology for science is a real philosophical possibility. On this view, well-known examples from the history of science become other than indicators of stupidity and ignorance. As Holton has pointed out in a penetrating paragraph related to this point, neither the work of Carnot nor that of Planck could be understood or appreciated until some time later.³³ It is doubtful that even great innovators such as these could fully grasp the signifi­cance of their own work, and its delayed acceptance by others can hardly be set down to their unwillingness to adapt to new ideas. To be sure, at some points in time a set of perceived anomalies given prevailing theory may make a new theoretical position widely appre­ciated immediately, or the success of some scientist in locating a much sought-after fact may be widely appreciated by his fellow researchers, but for many innovators significance must await the construction of related facts and theories.

Empiricism and rationalism have often assumed that we can de­scribe contemporary events completely. Cartesianism begins with the assumption that knowledge can be read from sufficiently clear and distinct ideas, and empiricism often begins with the assumption that knowledge can be read from sufficiently clear and distinct experience. We have already examined the difficulties with extending these po­sitions into comprehensive philosophies of science. It should now be clear that a view that narrative history of science is possible, that we can tell what is happening in science by describing fully what is hap­pening, is a deep and pernicious constraint on the philosophy of sci­ence, even where the philosophy of science is willing to concede the inadequacies of rationalism and empiricism. Once this is replaced by a subtler historical conception, the appeal of the dialectical approach offered here is transparent. Empiricism and rationalism have pro­ceeded by assuming either fact or theory to be fixed. In this way, they have captured part of what happens in science, but they cannot ultimately justify the assumption that their basis is adequately self- explanatory for the construction of methodology.

It is indicative of the scope of the problem confronted in this section that in some sense a narrative view of history is shared by Kuhn with his opponents. In a recent review of a book by students of Lakatos, designed to indicate how Lakatos’s philosophy of science can be sup­ported by history, Kuhn argues that “fitting the data” is a rather ob­scure notion in history as opposed to science.³⁴ Thus a resolute his­torian with a philosophical ax to grind can very well force the facts to accommodate his preconceptions. Kuhn also (and quite rightly) at­tacks the notion of “actual history” used by Lakatos as a myth about the history of science. The pool of all data relevant to history cannot be identified or surveyed. On the whole, then, Kuhn expects to find little of historical value in the history of science when it is written from an explicit philosophical perspective. Kuhn is quite explicit in his insistence that history cannot be intelligently written as a narrative chronological sequence of events, and yet he also feels that theoretical preconceptions should not be allowed to influence the perception of historical fact. What is a given for normal science, that theory influ­ences the perception of fact, is not to be carried over to Kuhn’s work as a historian. In history, the facts are said rather to be capable of speaking for themselves, provided that preconceptions are set aside so that the facts can be heard.³⁵ At least for history, then, some tra­ditional epistemological stance may turn out to be correct. Without endeavoring to describe how history can best be written, and without disagreeing with Kuhn’s remarks about philosophical history, it is still possible to suggest that the facts in the history of science do not speak for themselves. Rather, they must speak in consort with other facts (theoretical or experimental) if they are to say anything, and they will change in significance and relationships over time, or be lost from the historical narrative and cease to influence current vocabulary and per­ception.

The view of scientific history we have developed now makes it clear why science cannot be sharply separated from nonscience in general. At any point in contemporary scientific history, there will exist clear items of science and research groups whose efforts clearly fall within science. Yet at the same time, there will be nascent lines of research whose evaluation remains for the future. While some areas can clearly be regarded as science, any effort to sharply separate science from nonscience requires that the significance of new work, its more per­manent place in science, be assessed at the time that it is proposed. Any attempt to draw such a line by convention must inevitably lose the historical dimension of science, a dimension that is essential to its philosophical comprehension. The extent of new theory, its ability to accommodate data, will be determined over time, as well as the sig­nificance of data, their importance in adjudicating between theories. Data text in particular can be indefinitely expanded through interac­tion with reality. This feature of science is the major way in which it differs from nonscience, and it explains why the process of evaluation in science is never completed. The significance of data text becomes clearer as its context is increased through experiment. It may not last as significant in scientific practice, or its significance may be coded into scientific language or into scientific instruments. But a later text may suddenly shift the significance of an earlier one, and there can be no time limit on this process.