SOCIAL STRUCTURE IN SCIENCE

Social Norms in Science

One might suggest that the self-recognized best practice of scientists ought to be simply described, and this description offered as a char­acterization of scientific epistemology.

Whatever the relationship between sociology and philosophy, the use of sociological material here is entirely subverted to the ultimate end of philosophical analysis. Perhaps this will allay the xenophobia of philosophers who are too quickly dismissive or contemptuous of other disciplines. Sociological description is requisite for the social structure of science to become evident enough to allow for the de­velopment of a dialectical scientific epistemology. Ultimately, how­ever, there is a failure of such description that is not unlike the failure of closure encountered in traditional philosophical epistemologies. Just as the traditions of empiricism and rationalism cannot both explain important features of science—the crucial roles of both theory and data, for example—so the sociological tradition will fail to explain some important features of science. In seeing science as an institution, or as a culture, the revelations of sociological analysis must deal inevit­ably with features of science that make it similar to other social insti­tutions.

We can begin with the view that science is a social institution among other social institutions, and then apply various sociological tech­niques to study science as an institution. Scientists can be counted, their citations of one another noted, and in this way a certain amount of factual material becomes available to the student of the social struc­ture of science. The pattern of scientific social structure obtained in this way is very hard to differentiate from other intellectual social structures associated with nonscientific academic life. Literary critics make discoveries, cite one another, abandon various theories under the pressure of new evidence, and in many ways comport themselves in terms of social structure and private epistemology like scientists, except, of course, that they don’t on average have as much disposable income, and they are not generally thought to succeed in locating objective knowledge. The former is an accidental fact that can hardly explain the latter.

This external structural approach to science can be sharpened by looking for the institutional norms of scientific behavior, violation of which produces sanctions by other scientists. An early and widely cited attempt to do this was made by Merton, who found a set of norms that he took to be characteristic of science from the seven­teenth century to the present.² Merton has been attacked on the basis that the norms of science have noticeably changed over this period of time, but another issue seems much more important.³ Although Mer­ton’s norms are grouped differently in different texts, making quota­tion difficult, a fairly differentiated list can be cited as follows:⁴

Faith in rationality

Universalism (All scientists have equal claims to the discovery and possession of rational knowledge.)

Individualism (Science is antiauthoritarian.)

Community (Credit for discovery is given to individuals, and se­crecy about results is immoral.)

Disinterestedness (Self-interest is achieved through community rec­ognition.

Impartiality (The scientist is interested in pure knowledge, not in applications.)

Suspension of judgment (Evidence is the only arbiter of truth.) Absence of bias

Group loyalty (Production of new knowledge by scientists is sup­ported over guidance of research by economic interests.)

Freedom (Control of scientific investigation is regulated only by epistemological considerations.)

The norms are somewhat condensed and overlap too much in any such summary, but their general import is clear. Certainly these norms have some relationship to science, and yet it is manifest that they are frequently violated in fact, and that violation need not lead to the imposition of sanctions. It would, however, be a mistake to dismiss these norms as simply providing an overly idealized and mistaken picture of science. These norms portray the picture of science that many scientists prefer to see as the public image of their profession, and that many scientists believe they follow when they are doing sci­ence. But these attitudes may betray a lack of self-consciousness on the part of the scientists evincing them, although this is perhaps dif­ficult to see at first. This set of norms can be thought of as standing to science as its ideology, and the attitude of many scientists to this ideology can be thought of as a (necessary) form of false consciousness that aids concentration on scientific work.

To see what is meant by this, we can imagine that some medieval theologian is working on an interpretation of, let us say, a book of the Bible. In doing this, he may (privately) want to show that his knowl­edge of the Bible and his insight into its meaning is greater than that of any of his rivals. His quest for status is not undertaken through physical violence against his rivals, nor can he be successful just by claiming greater insight. There is a physical and largely determinate text to be dealt with, and a variety of background constraints of an intellectual and theological nature to be satisfied.

The case of the scientist with respect to rivals seems not all that dissimilar. A scientist will pick a problem that seems soluble to him or her, given background, available equipment, and so on, as well as one whose solution is estimated to be associated with the desired recog­nition and status. So much goes without saying, and the scientist may not consciously recognize this fact, simply because everyone behaves in a similar way. As in the case of the theologian, success depends on background constraints not within the control of the individual sci­entist. There are recognized experimental standards, a background set of plausible theoretical possibilities, and there are standards of scientific exposition and debate to which the Mertonian norms are relevant. Scientific status is sought by a procedure whose social inter­action is governed by the Mertonian norms. A scientist may be vain and arrogant, but his successful public performance depends on treat­ing all other views only in terms of their experimental support and theoretical consequences. Public science and public theology are then played out against a set of recognized professional standards, stand­ards that are not to be compromised by the personal goals of the participants. The Mertonian norms are, so to speak, the rules of the game.

The Mertonian norms have in recent years been confronted by the recognition by some scientists that human motives play an essential role in scientific research. Watson’s The Double Helix is an outstand­ing example of expose literature, and was perhaps the first book to explicitly acknowledge the role of personal goals in motivating scien­tific work.⁵ In this autobiographical account by one of the discoverers of DNA structure, jealousy that a distinguished scientist might achieve the result first, spying on that scientist’s work through an intermedi­ary, and outright secrecy about personal results all play a role.

The fact that the Mertonian norms rule public science is quite con­sistent with greed and passion, or impartiality and fair play, at the personal level. Ravetz has suggested that the recruitment of scientists from wider segments of society is having an influence on the type of person who is becoming a scientist.⁶ Although motivational factors in the performance of the highest-quality scientific work of which one is capable are subtle and complex, a sheer shift in personality type is compatible with continuous quality in scientific work, provided that the public norms of conduct can be preserved in scientific contro­versy.

In many areas of active research in science, pairs of scientists can be found who disagree on some specific proposition. Typically, the scientists who disagree will make quite different simplifying assump­tions in order to construct the models from which they draw conflict­ing conclusions. Each scientist in such a dispute may believe the other scientist to have made mistaken or unilluminating simplifying as­sumptions, but as all simplifying assumptions are recognized as such, and as the full range of consequences may not yet have been drawn from these assumptions, it is not necessarily part of the scientific dis­pute to quarrel about these assumptions.

Mertonian rules thus seem to bear an analogy to proper courtroom procedures between adversaries. They are not necessarily to be found in the individual pursuit of scientific knowledge, but they do constrain the cultural products of science, research papers and books, for ex­ample, and they also constrain the public debate at the heart of sci­entific progress. Mertonian public norms revolve around full disclo­sure of experimental results, or at least around the idea that no false statements about experimental results will be publicly disclosed. Sci­entists are tied into a network of other scientists, and the work of other scientists must be trustworthy if the system is to continue to develop at a satisfactory rate. Mutual trust would be subverted by cheating. A scientist could manufacture results, or not reveal results that were incompatible with his or her favorite results, and this has happened. But on the whole, scientific morale has remained high, and cheating (even if it is increasing) has been rare enough to provoke scandal and notoriety where it has been discovered. What is the mech­anism that brings this about? The mere pledge to uphold Mertonian ideas or the assertion that these ideals are to be observed in public discussion is not explanatory. Pledges that are at odds with the exi­gencies surrounding personal gain will inevitably give way to pruden­tial calculations. Workers in a factory may make various work pledges quite at odds with private intention, and break the pledges at the first reasonable opportunity. Workers may desire the most pay for the least possible effort, the reverse of the employer’s objectives.⁸ On the other hand, scientists consistently strive for the best work they are capable of, and we need to find the differentia between the profes­sions and the scientists as well as the differentia between workers and scientists.

Two factors seem of crucial importance in explaining scientific mo­tivation to do the high-quality work that is consonant with institutional goals. One is that a scientist works at a single problem for a pretty long period of time, typically, and can be expected to make only a few significant discoveries in a lifetime of work. The relationship be­tween the scientist and his work is thus found on a time scale where a scientist can expect to take personal pride in a good piece of work. The discovery or result will be his or hers, given the reward system of science. Scientific work thus shares a relationship with artistic work, or craft work, in which the signature of the producer is regarded as part of the work and may function as a sign of worth and quality recognized by others. If quality work is the goal of science, the reward system for the individual is consistent with the institutional goal, and puts pressure on the individual to produce work that can be defended in the public arena as a contribution to science for which he or she should receive recognition. The other important factor is that science embodies a social structure in which each individual can imagine a constant chance for personal recognition. From one point of view, science possesses very little hierarchy, It is fragmented into research areas within which there are recognized stars (of perhaps approxi­mately equal magnitude) and the rest of the researchers. A Nobel Prize winner may be an important physicist, but the same prize win­ner may also be irrelevant to a research area in which there have been no Nobel Prize winners. Workers in this area need not see the prize winner as standing above them in a hierarchy. Each scientist may thus imagine that one good piece of work is all that it would take to achieve scientific eminence, at least among those working on some well-de­fined research topic. By comparison, the factory worker is typically resigned to remaining in his or her position, or one like it, since the pyramid of company offices leading to president is a constant and visible reminder of the difficulties of rising through the hierarchy. In the professions, the typical professional is practicing the profession as a source of superior income, and no system of recognition (except for local social hierarchies) exists that would motivate the search for ex­cellence in practice. Excellence under these circumstances must be pursued on personal grounds, or because it is somehow expected to attract superior clients in the long run of one’s career.

The social structure isolated here does not begin to explain the objectivity of scientific knowlege. It is designed merely to illumniate why cheating is so scarce in science, that is, why individual and in­stitutional goals are so remarkably consonant in practice. Merton’s norms are what would be expected in a system of such consonance on individual recognition. We can say that in the past, science as pursued primarily by individuals maintained a reward system in which the possibility of recognition for everyone who did good work was com­plemented by individual attempts to do good work. The institution and the individual were in harmony. Structural changes seem much more threatening to this system than any suspected lessening in the personal qualities of scientists. The cheating scientist of the past had to restrict himself or herself to minor league work, or risk a substantial chance that dishonesty would be discovered in repetition of the works, when the original results could not be defended, since the thread of responsibility was securely anchored at one end in a particular person.

The move to big science threatens the stability of this system. Within a scientific team cheating may be encouraged in lower positions be­cause of a political pressure to please one’s superiors. In the team situation, the lower positions will often be filled by persons knowing that the recognition for success will go primarily to team leaders. They thus lose the pure motivation to do good work, and are subject to political suasion, unless they belong to a team whose leadership creates the atmosphere for top-to-bottom quality, and whose recruit­ment of talents and personalities is lucky. In those research areas where large funding is requisite, those scientists or teams of scientists who are not able to secure funding essentially lose their chance for recognition. Recent years have seen squabbles and studies of the way in which scientific grant monies are administered. There is not enough money to fund everyone who would like to do expensive research, and those who are not funded have to shift research interests in many cases. Attention under these circumstances will be shifted to research projects that have a good chance of being funded, rather than those that might be chosen on purely scientific grounds. It is possible, of course, that these motivations could coincide, but frequently they will not. Whitley reports that a physics research laboratory receiving gov­ernment funding may spend up to half of its time replicating experi­ments in order to produce research reports, such reports being the government’s criterion of scientific productivity.⁹ In this way, time and labor can be deflected from pure research. For those who are losers in the funding game, morale may be difficult to sustain. Big science, necessary for economic reasons in many areas of research, threatens the personal award system that seems to have played an essential role in preserving the consonance between personal moti­vation and scientific goals that has characterized the explosion of sci­entific knowledge for over two centuries.

It may seem that this brief look at social norms in science has not advanced our topic at all. If science is seen as a public struggle for recognition played out according to certain internal social norms, is it not true that this is true of all academic disciplines? Let us return to our notion of science as containing two levels of texts. In the human­ities, the important texts are set by tradition, they are small in num­ber, and the scholar is always confronted with several existing and presumably plausible prior interpretations. Even when a new inter­pretation is added to this array, choice among them depends on feel and insight. One cannot force recognition of the validity of one’s inter­pretation. It is possible, of course, to try to write new texts, but the vagaries of fame tend to preclude this as a reasonable route to success, and simply attempting to fix up flawed but existent texts is not re­garded as original, even where it is legitimate. In science, opportu­nities beckon. One can write new text, interpret new text, or pursue a variety of other activities such as emending or otherwise improving existent text. The existence of these opportunities would not only explain the historical high quality of scientific work in all fields of science, but also offer a basis for a distinction between scientific work and work in other academic disciplines.

Cognitive Norms in Science

A different sociological approach to science is to regard scientists or groups of scientists as constituting a special society or community with its own associated culture. Science is not then regarded as an insti­tution within a given society, but as constituting a society in itself. Instead of comparing the institution of science to other social institu­tions, one could then attempt to describe the internal culture of sci­ence and scientific subgroups. Kuhn’s well-known book, The Struc­ture of Scientific Revolutions, approaches science in this way, although for Kuhn science turns out to be less a total society with an associated culture than an assemblage of fairly small research societies or groups each of which is unified in direction and values by background para­digms.¹⁰ Like members of any culture, the members of a research group cannot fully articulate the sources of their unity of outlook, since the consensus is partly the result of sharing a research activity that is not itself fully and consciously spelled out in all of its details. If this view that the sources of consensus can’t be articulated is cor­rect, incidentally, it spells defeat for any program attempting a neutral description of scientific practice. The fragmentation of science that results from this view is inimical to philosophical generalization, since the practices of each research group will make sense only against its particular paradigmatic background. Scientists are constrained in per­ception by this background according to Kuhn’s account, and perhaps this is why Kuhn’s approach has not been widely admired by philos­ophers.¹¹ They tend to see scientific activity as no longer fully free and rational if it is governed by paradigms, since paradigmatic back­grounds may be taken to function as an inarticulate and hence irra­tional authority. The moment a paradigm could be spelled out, it could (and presumably would) be open to rational discussion and con­sideration of alternatives, and would have lost its constraining force. Paradigms, if they could be articulated, would be acceptable to phi­losophers, but they could no longer play the role in scientific research that Kuhn spells out. At the same time, many scientists have wel­comed Kuhn’s account, and they seem unmoved by the philosophi­cally ominous inarticulate properties of a paradigm. Their willingness to accept Kuhn’s account may be partly because Kuhn’s account makes scientists a breed apart, and scientific expertise something that can only be achieved by a long process of training that resembles a process of acculturation. Pure scientists, especially, like to view their work as autonomous with respect to other forms of social activity, and Kuhn’s account allows them this luxury.

The scientific norms established by paradigms are basically cogni­tive norms in the sense that they constrain scientists in their cognitive activity toward a consensus on the significance of formulae, instru­ments, and experimental data. In practice, Kuhn’s exact account of par­adigms has wavered somewhat. Originally, Kuhn took paradigms to be the entire background set of values and attitudes of a scientific research group, as well as the particular formulae and exemplars (standard ways of connecting theory and formulae to experimental arrangements) characteristic of the research group. Lately, the sense of the term paradigm has been narrowed to that of exemplar, but the general conception of consensus in unifying a research group remains the same. For Kuhn, paradigms constrain the members of a research group to act similarly in approaching nature, and to expect their in­teraction with nature to proceed along certain anticipated lines. This allows a division of labor to occur in which scientists can cooperatively pool their efforts because they needn’t argue about fundamentals, hence allowing progress to occur. Greater consensus over paradigms, as in physics, allows homogeneous research groups to participate in an ac­celerated attack on common problems.

During periods of normal science, scientific activity proceeds by solving new problems in the manner sanctioned by the paradigm, and in developing experiments to extend the paradigm’s range of appli­cation. This has the interesting twist that the power of the paradigm to constrain thought means that a result not fully expected within the constraints of the paradigm is at first taken as a signal to the scientist that the experiment involved was poorly designed, not that the par­adigm might be wrong. This observation jeopardizes the simple logic of falsification that philosophers find so congenial, and means that the reaction of good scientists to an experiment can’t be predicted by mere logic. The idea that an outsider point of view could determine how scientists should react if they are fully rational is irrelevant to the actual practice of science. What scientists see as plausible and rele­vant is determined by a space created by a paradigm, not by a space created by logic. This account is therefore compatible with what was said in the last chapter about logical space in connection with scien­tific explanation. To understand a research group, some knowledge of the content of its paradigm or paradigms is essential in the Kuhnian reading of science as scientific culture.

Reactions to Kuhn have been sharply divided between complete rejection sometimes expressed in various reasonable objections to the sketchy account of research groups and paradigms offered in his book, and acceptance followed by an attempt to spell out the relevant par­adigms for various research groups, or even for whole disciplines. There is no doubt both that Kuhn’s account was the first really in­sightful description of everyday scientific activity and that it contains serious flaws. The Kuhnian account of research groups suffers from the general drawback of functionalist descriptions of social groups, which tend to make such groups seem both more uniform internally and more distinct externally than they actually are. There is in fact both violent internal disagreement within the research groups met in science and hot argument between research groups ruled by different paradigms. The former is bloodier than paradigmatic unity would sug­gest, and the latter ought not to take place with the vehemence it does if adherents to different paradigms should find each other’s at­titudes and work incomprehensible and even nonscientific. Because research groups are too internally uniform on Kuhn’s description, he is forced to hold that when anomalies pile up sufficiently against a paradigm, only a revolutionary escape to a new paradigm is possible, and once this is accomplished, or once new people have populated a new research group, rational communication between the old and new research groups would be impossible. Kuhn’s account, based on total agreement inside the group, leads inevitably to this end. It is clear that his original account overemphasized the uniformity of opinion within a research group, and that a more evolutionary account of progress is required in which scientists within research groups sharing the same paradigmatic exemplars may have markedly different out­looks, and in which talk between research groups is possible, includ­ing fruitful discussion between scientists who are utterly at odds about the assumptions and models involved in their work. An improvement on Kuhn requires seeing that the individual scientist usually doesn’t have grand goals except in philosophical moments, but rather he or she is working on some quite specific problem to which a solution can be hoped for in the near future. To solve it, the scientist may try a wide variety of approaches in a relatively short period of time, and change his or her theoretical outlook repeatedly, something that is not quite compatible with Kuhn’s original account.

The main stream of scientific history, as well as the large revolu­tionary shifts in scientific opinion that occur occasionally and affect many scientists, has to be reconstructed from a detailed history in which people are not quite sure where they are going, or how they are going to get there, or what the significance of their work really is. That a more evolutionary account seems to fit scientific practice better is shown in various studies of scientific specialties, of which one by Crane is extremely interesting.¹² Crane looked at theoretical high- energy physics during the fifteen-year period 1960-1975. Physics, of course, should exhibit Kuhn’s account most clearly, since he devel­oped his account partly to explain the apparently rapid progress in physics in comparison to other scientific disciplines. Theoreticians during the period in question sought to explain what they called weak interactions, strong interactions, or both. Crane found more than twenty different lines of inquiry into these phenomena to have attracted the­orists during this fifteen-year period. She also found a quite compli­cated pattern of influence between these lines of inquiry, with sci­entists having shifted allegiances repeatedly, partly because of experimental results, and apparently partly because of sheer fashion and intellectual boredom. During this period there were several un­expected experimental findings, but only one real anomaly (charge and parity violation). This tends to cast doubt on the idea that theo­retical progress comes through periods of revolution, and that revo­lutions are a response to a large stockpiling of anomalies. Further, Crane found that the entire area of theoretical high-energy physics accepted certain symbolic generalizations related to relativistic quan­tum mechanics, and also accepted certain general values (testability and elegance) for evaluating theories. Individual scientists in the area accepted various metaphysical models quite independently of their line of inquiry, but exemplars (in Kuhn’s sense) were held in common by those involved in a given line of inquiry.¹³ Crane’s research sug­gests a much richer pattern of grouping than that proposed by Kuhn.

Kuhn’s method of description emphasizing paradigms approaches a phenomenon we noted earlier from another direction. The thinking of scientists is highly constrained by background scientific assump­tions, not all of which are totally conscious, and this may seem irra­tional from a philosophical point of view, unless it is realized that these assumptions are made at a level of particularity that has been worked out in close interaction with the phenomena being studied. Scientists participate in some diffuse cognitive attitudes, such as a faith in the fit between mathematics and the world, a belief that fun­damental processes can be understood by the human mind, and so forth. Also, because of the way in which the sciences are divided in the universities, the journal systems, grant-giving agencies, and so forth, scientists will see themselves as physicists, organic chemists, and so on, and will share some disciplinewide attitudes. All of these background factors will play some role in scientific thinking. But at the daily level of work, the important factors will be that so-and-so has obtained such and such results with this method, that so-and-so has obtained what seems a suspiciously accurate result using a device that normally gives results difficult to replicate, and so on. That is, day-to-day scientific thinking will be most constrained cognitively by a knowledge of what other scientists are doing, what processes have brought what significant results, and so forth. The notion of a para­digm is a convenient way to capture this, but the associated picture of science as fragmented into internally consistent research groups ruled by paradigms who find one another incomprehensible and who occasionally destruct when too many anomalies pile up, to be replaced by new groups, is simply too crude a sociological picture of science to serve as anything other than a first approximation. As a first revision, we need to note that although paradigms may constrain the direction of research quite decidedly, research groups will often contain mix­tures of individuals who disagree on various matters (how to go on) even though they do agree on the values ensured by the shared par­adigm. For example, for one scientist a new and more careful exper­iment testing an old idea may seem preferable to the experiment testing a new idea favored by another, even though both can agree that with sufficient time and resources, both steps would be desirable. Further, and this is crucial, a mixture of divergent thinkers may be quite essential for the stimulation leading to creative advance.

Kuhn’s account overemphasizes the power of pardigms to coerce thought. He gives examples of how hard anomalies are to notice, and compares this process to perceptual studies in which expectation makes it difficult for a subject to notice certain things.¹⁴ If theory determines observation, and if paradigms determine thought, how can anomalies be noticed? The answer to this puzzle lies with a human ability to grasp several paradigms more or less at the same time. Just as an anthropologist may be native to several cultures, and have the ability to evaluate some event from several different cultural perspectives, so a scientist may be native to several paradigms. Scientists move from research group to research group. Two scientists from different prior groups joining the same research group will not internalize ex­actly the same paradigm. They may construct new paradigms out of a sensible fusion of elements of the old and the new, so that paradigms need not spring full-blown into view after revolutionary periods, and scientists may come to realize that one paradigm is more globally satisfactory than another, even though the view from the two para­digms is quite distinct.¹⁵ Kuhn, by making paradigms totally distinct from one another, makes it seem unlikely that one could lose its grip on a person and be replaced by another. Kuhn’s scientists are as dull as Cartesian robots, consistent machines lacking any capacity or in­stinct for playing with a variety of viewpoints. This seems false to human psychology, and to the fact that scientists successfully migrate from one research group to another and require only a short period of time to readjust. The correct insight is that paradigms are specific to problem areas and are not fully articulate. This allows a small group to communicate fully through language that is partly symbolic, since its meaning depends on a context not shared by outsiders to the prac­tice. This full communication implies a small group, common experi­ences, common understanding, and perhaps a special language coding these shared features. This shared full communication seems a req­uisite for scientific advance at the microlevel. Any attempt to spell out the paradigm, say, at the level of a Scientific American account of a discovery, loses this symbolic dimension of group language, and makes the thought of the group seem simpler and more obvious than it really is, since the shared subtleties of understanding, what is per­mitted and what is forbidden by the techniques, the data, and so on, are either stripped away or lose plausibility in gargantuan formula­tions. The same process occurs in the preparation of the research report, where full disclosure of background assumptions would swamp the vital information in a sea of irregular assumptions well enough known to those for whom the report is written.

Much of the discussion surrounding Kuhn’s views has been related to the fact that the level at which they are intended to be applied remains obscure in his work, and no precise formulation seems to fit all the relevant epochs of the history of science. Copernicus, Darwin, Freud, and Einstein are all associated with scientific revolutions that originally occurred within small research groups, but had far-reaching consequences for views held in everyday life. Many people found these views difficult to accept, and many people never accepted them. Yet they do fully deserve the title revolutionary. It is not true, how­ever, that no older scientists could accept these new paradigms, and that they triumphed only when they were adopted by younger sci­entists, as Kuhn suggests in his book.¹⁶ All of these revolutionary ideas were accepted by at least some scientists in every age bracket, and even though older scientists were dying off at a higher rate than younger scientists during this period, there is no reason to suspect that ideas kill older scientists, or that the death of older scientists facilitates the spread of ideas.¹⁷ Age cannot be even the major explanatory factor for acceptance or resistance. To be sure, older scientists are likely to have intellectual capital invested in older ideas, but on many grounds they might choose to accept a new set of ideas, even on the grounds offered by reason and argument. For younger scientists, the seemingly nat­ural view that they are inclined to leap toward new ideas encounters problems. A young scientist seeking to establish a reputation might decide either to work in the area of a new paradigm in order to chal­lenge received opinions, or to make some piece of work more rigorous than ever before by carefully redoing the past. On the whole, the young are likely to differ from the old, if only because of the impre­cision of education as well as the fact that education is set against a different social background over time. A modern scientist might con­sciously choose to pursue some work of ecological significance without comment, but such a choice would not have been so natural to con­temporaries fifty years ago. It is hardly credible to assert that new Ph.D.’s do not have minds that are as well stocked as older minds, and hence are likely to be attracted to more speculative ideas because they don’t perceive the lack of solid scientific support for them. Clearly, a young scientist may choose to pursue a wide range of strategies in developing a scientific career. If age does not play as important a role in connection with revolutionary new paradigms, as Kuhn has sug­gested, it becomes of questionable significance in a modern setting, where a scientific revolution has significance primarily for valuations within some scientific specialty, and hardly confronts major world views. Here a successful new paradigm may reorganize thinking or open new avenues of research in a manner accessible to those working in closely related areas, and rapid adaptive switches and conversions may be expected along with internalization of the new paradigmatic outlook. Much of the apparent excitement of Kuhn’s views seems to result from an unnoticed transfer of the significance of the few huge revo­lutions in scientific thought that affected human world views in an earlier age of science to revolutions now occurring in connection with research groups within ordinary scientific advance. These are the lo­cus for Kuhn’s considered views about scientific progress that do not entail wild relativism or incomprehensibility theses, mostly because paradigmatic views are located within the confines of disciplines that have research groups oriented to recognized objects of inquiry, set­tled styles of experimental and theoretical attack, and a variety of associated stabilizing values. Relativism and incomprehensibility will be found in research on extrasensory perception, UFOs, and wher­ever a disciplinary anchor is not available and people may approach a given problem from any direction whatsoever.

One thing Kuhn has in common with his philosophical critics is a reliance on the idea that the history of science can be written as a history of scientific ideas and the way in which they have changed over time. The succession of scientific ideas must be related to the succession of scientific instruments, and without such an underpin­ning in data the notion of shared paradigms and exemplars cannot be fully fleshed out. What seems possible and impossible to scientists, especially where this is intuitive and only partly articulated, is fre­quently linked both to actual experiments and to the agreed results of thought experiments in some research area, and these constraints will not appear explicitly in the theories or papers of a research group, nor need they be agreed on by all members of a research group. Quantum theory is a good example of a physical theory that has de­veloped to fit a space provided by experimental results that at first seemed odd, and then came to be the only results expected.¹⁸ Here accumulating experimental results seemed to have gradually forced a quantum consensus outlook onto scientists who felt that they could interpret the experimental devices classically, and who gradually came to share similar attitudes about interpretation of the data obtained from these devices. This is quite the opposite of a consensus forming that was then elaborated in experimental testing. An important fea­ture of scientific instruments and experimental techniques is that they reduce the variety and complexity of actual situations to a few man­ageable results, most of which can be numerically recorded. If we grant that observation may be influenced by background theory and background theoretical expectations, the fact that observations are transferred through instrumentation serves to detach the value of ob­servations from the hopes and expectations of the scientist. Rather than making simple interpretations of complex objects, scientists tend to make complex interpretations of relatively simple objects. Instead of reacting to an entire process, a scientist reacts to some numbers or some feature of a process that he will accept in common with other scientists who may have quite different interpretations of the same process. The atheist and the theist react to their entire experience of the universe with conflicting claims, but two scientists may react to a single number representing some experimental datum by tracing quite different consequences from it in the context of two quite diverse and complicated theories. Instruments and techniques assure scientists that they are talking about the same thing, that is, some scientific fact, when they disagree. On the other hand, it is questionable whether the atheist and the theist inhabit the same universe. Positivists sought for certainty in scientific observation, but they overlooked the possi­bility of grounding community of understanding in science on instru­ments and techniques. The progress of science is really the progress of instruments and techniques. Better instruments and techniques tell us more about the same universe, and hence they frequently force changes in theoretical outlook. In this sense, there is positive progress in science even though theoretical interpretations may undergo wide flip-flops, what is taken for granted at one time being questioned for a while and then taken for granted again.¹⁹ At times, new instruments and techniques may reveal unanticipated constituents or aspects of the universe. This is why progress isn’t cumulative, and data may become worthless. At times, new interpretations may shift the signif­icance of data, making crucial and important certain data that were previously considered of marginal significance, but this will not in itself change the values of agreed data. The fact that perception is determined partly by expectation is combated in science through in­strument and technique, which tend to establish data that can stand independently of theoretical outlook, even though the data may not be neutral on which theory can most likely be projected onto new data in an area of research.

Kuhn’s view, like that suggested in the last chapter, entails that there is no sure test for progress at the microlevel of scientific prac­tice. Paradigms replace one another, but one cannot say whether a given replacement is a mistake or not, or whether it gives greater insight into the workings of nature. Later on, the path to the present will be clearer, and what is progress can be measured as significant steps toward the present. In response to critics who charge that this account makes scientific knowledge relative or subjective, Kuhn has suggested that progress just is what happens in scientific history, so that criticisms based on his failure to provide a criterion of progress based on gradual approximation to the truth fail because the critics are also unable to specify what approximation to the truth can mean, and are hence unable to provide a test for progress at the microlevel of scientific activity.²⁰ But science can’t really be taken to progress as a result of a series of revolutions in thought, and both Kuhn’s view and that of his critics have overlooked the importance of setting ideas into a context of scientific experimentation. That scientific history is not punctuated by revolutions in Kuhn’s sense is evident from the fact that older theories have survived revolutions to take a place in science along with newer theory. A good example of this is that New­tonian physics is still a good physical theory and is studied by students of physics even though Einsteinian relativity theory has replaced Newton’s theory in many physical applications as a deeper insight into nature. Similarly, classical physics has survived alongside quantum physics, and in many cases is used along with quantum theory in the explanation of experiments, although, once again, quantum physics is regarded as providing deeper insights into nature. Both of these pairs of theories are logically incompatible even though one may loosely be regarded as an approximation to the other under certain circum­stances. It is sometimes argued that although the approximated theory is false, it is used for pragmatic reasons to give suitable answers when great precision is not required. In contrast to Newtonian and classical physics, however, phlogiston theories have disappeared. The differ­ence once again requires a reference to the missing factor of instru­ments and techniques. As long as naked-eye observations and simple techniques and instruments are employed on human-scale objects at low differential velocities, in other words, as long as the data are restricted to the only kind of data that could be gathered by scientists given their instrumentarium until the twentieth century, classical physics is a vast, conceptually simple, interlocking, and consistent system expressed in a language that is perfectly precise and accurate with respect to the suggested data.²¹ The phlogiston and impetus the­ories were set against a quite modest and imprecise data basis by comparison. It is no wonder that they were less robust in the face of new data and competing theoretical explanations.

Scientific Disciplines

The pure scientific disciplines seem easy to list in terms of their re­lationship to the modern university curriculum. Physics, chemistry, and biology (possibly geology) are clearly scientific disciplines, and both psychology and sociology claim scientific status as social sciences. Branching from chemistry and biology are the partly applied disci­plines of biomedicine and agriculture. Mathematics may or may not be regarded as a science, but applied versions occur as disciplines with putative scientific status in engineering and economics. History and political science may also lay claims, at least in certain forms, to scientific status. This basic structure is, of course, the structure of university science, and the identity of scientific disciplines is tied up with the extensive development of modern science in the nineteenth century as part of the modern university. At present, chemistry, en­gineering, and biology departments are usually divided (at least in the larger universities) into departments constituting such subdisciplines as polymer science, electrical engineering, and botany. The inevitable ossification of university structure has made it difficult for some new disciplines seeking scientific status, for example, computer science, to find a clear place in the university structure. Sophisticated analyses of citations and key words in journal articles tend to support this well- known informal structure of disciplines, and that is not surprising, since both scientists and their journal editors tend to view scientific work as grouped into these traditional disciplines and associated emergent subdisciplines.

It is clear that one could begin research on disciplines with scien­tific papers and analyze the references to past work contained in them. The details are complex, because the pitfalls are nearly obvious to inspection. Explicit reference to sufficiently well known work is not necessary among scientists, and it is not clear when explicit references indicate a genuine intellectual debt or conceptual linkage, rather than attempts to take a wide range of literature into nominal account. De­spite problems related to these and other observations, different stud­ies have found the same gross structures in the literature. If one starts with an intuitively related set of papers, citations in the papers tend to close in on themselves so that papers can be grouped in clusters whose authors constitute research groups in the sense that we have been mentioning. These clusters can in turn be subdivided by strengthening the citation criteria required to code influence. By studying the literature from a selected list of journals in chemistry, physics, and biomedicine, for example, investigators have found that physics is largely separate from chemistry and biomedicine, but bio­medicine and chemistry have an important overlap in which, for ex­ample, literature on the structure of hemoglobin is not clearly chem­ical research or biomedical research in the eyes of its participants.²² Biomedicine, in fact, contains a huge number of clusters that are harder to separate, since biomedicine contains many review and method ar­ticles that are cited by clusters not otherwise citing the same litera­ture, and these must be ignored to achieve cluster separation. These studies also show that chemistry lies between physics and biomedi­cine in that the links between physics and biomedicine are not as strong as those between physics and chemistry and between chemis­try and biomedicine. Citation research confirms the standardly per­ceived structure of scientific disciplines, and also confirms the Kuhn­ian insight that scientists (and their documents) can be clustered into small groups with high cognitive cohesion within the groups, the members of which are attacking some fairly specific scientific prob­lems, although citation research can’t by itself confirm the idea that Kuhnian paradigms cause group cohesion.

What is somewhat more surprising is that intuitive differences be­tween scientific disciplines often thought to exist do not appear clearly in the data when these disciplines are studied using citation research. For example, many people hold the opinion that physics is a paradigm science, but that sociology stands somewhere between physics and philosophy or between physics and literary criticism. One aspect of this belief is the view that physics has progressed at a much greater rate than sociology has in the last century. A measure of such a belief would be the age of citations. One would expect citations in physics to be to papers that are not very old, so that recent work in physics is more likely to be cited than older work, but statistics measuring this phenomenon show that all of the sciences have a similar reference pattern in terms of the age of citations, and there is a sharp break only between all of the putative sciences and the humanities in terms of reference patterns, the humanities averaging much older reference dates than the sciences do.²³ Within disciplines, subdisciplines and research groups can vary considerably in citation patterns. Certain areas of experimental psychology will tend to cite only very recent work, and other areas, such as clinical psychology, will cite at least some older work. This pattern of differing citation age in subdisci­plines is true for all of the sciences, although disciplinewide averages vary little. The result is that the scientific disciplines show a remark­ably similar citation pattern in statistical analysis. The differences be­tween the sciences, or even average differences in some sense, that are intuitively thought to mark cognitive distinctions in paradigm structure between disciplines seem (at least so far) to elude statistical technique.

The social structure of scientific disciplines we have analyzed so far is then something like this. Scientists are grouped in universities, and identified in other research institutions, according to recognized sci­entific disciplines that have developed historically along with the uni­versity system. Disciplines can be analyzed into subdisciplines, and then into research groups. Research takes place primarily within these small groups, which are aware of other groups working on the same or similar problems. The direction and style of their research is de­termined at least partly by what these other competing groups are doing. Within such groups, and between a small number of them, full exchange of scientific information is possible because of a shared feel­ing for the nature of the data, the available techniques, and so forth. This is therefore the crucible within which scientific progress takes place.

Scientists may communicate with scientists outside their primary research group, and such communication may be quite fruitful and provocative in the sense that it may give a scientist a view of what is happening elsewhere and provoke ideas of potential value for his or her own research. This casual communication is widespread in sci­ence, and quite loose, as when colleagues simply chat about what is going on in their respective fields.²⁴ From time to time, a new idea or technique of considerable promise will be developed by a member of a research group, and this will begin to draw the attention of other scientists. Increased communication between the scientists attracted to this idea and either recruitment of other scientists or the weaken­ing of ties to them will create a cluster of scientists operating with this new idea, or paradigm. These scientists, of course, may be at various institutions, but they can collaborate on research, and they may actively recruit students or younger members of the profession to pursue similar lines of research. The new work will appear in some journal and trigger, if it is successful, a flurry of articles in increasing numbers that pursue the same themes. In time, a successful cluster may form the basis for the creation of a recognized specialty within a discipline.

A process of the kind just described bears some relationships to Kuhn’s account of science, and some differences. The new paradigm need not arise from a revolutionary crisis and a break with older sci­ence, rather it will typically appear as a locus of new interest within a discipline already sharing various values, and its potential interest will be clear to at least some discipline members. After initial suc­cesses, the cluster need not give way to a revolutionary break. Rather, as a specialty, it may have great longevity within a field in spite of (permanently) recognized anomalies and difficulties. The rate of con­tributed literature will settle down, and perhaps decrease, after initial successes, but the sequence of Kuhnian revolutions need not occur. Rather, what happens is that good scientists become interested in a new project and soon switch to that, leaving second-rate scientists or cautious personalities in command of the older ship. The background context of a scientific structure within which paradigms can develop, flourish, and turn into recognized specialties is missing in Kuhn’s ac­count, since he chooses to notice homogeneity only within the para­digm groupings.

The way in which research groups form around topics of interest, become solidified into permanent specialties, and shift membership is not structurally different from the way in which human groups of all kinds form to attack problems, and it is not unique to science. In many cases, people who form groups have such disparate backgrounds that the problem to which the group is directed and certain values concerning possible solutions are the only common denominator of group members. Early promise or early successes will hold the group together, but the group may disband or achieve some steady-state structure as the problem is solved or is seen to require constant at­tention. A group of ordinary citizens forming within a city or town to address some topic of mutual concern may show this dynamic. What is different about a scientific research group is not its internal history in this sense, but the scientific background against which it arises and against which it dissolves or turns into a permanent feature. Progress is not so much consensus, or the enforced unity provided by a para­digm, since many human groups are unified in terms of goals and strategies, but the fact that research groups recognize their position in the framework of a scientific discipline, with which they share fun­damental assumptions.

Few human institutions have been large enough, sufficiently well organized and divided (conceptually), to offer this opportunity for re­search groups to intensify in order to work on a problem of generally recognized significance given the background institution. The theo­logical organization of the medieval churches perhaps provided such an opportunity, but with a difference. Science as an institution is poly­centric, and as we have seen, it does not interpret fixed texts so much as it constructs and interprets new scientific texts through interaction with nature. Polycentrism is an important aspect of scientific struc­ture. There is no doubt that the polycentric competition of universi­ties and research institutions in Germany, England, and the United States has contributed to healthy science, and there is some suspicion that the relative lack of polycentric structure has hurt French science. Science is, of course, at the same time elitist. A few scientists make a disproportionate contribution to the literature, and only a few sci­entists can gain wide reputations outside their own scientific specialty and disciplinary contacts. Polycentrism allows this chance for fame to appear in a variety of places, so that every scientist is potentially close to the opportunity for achieving a wide reputation, a fact of some importance, as we have seen, for morale. Polycentric structure thus quite naturally replaces the struggle of individuals for recognition, the process that preceded institutionalization. It is possible to imagine motivation sustained in a social structure in which the status of sci­entist is one of the few opportunities for superior financial and polit­ical status, so there is probably no essential connection between healthy science and polycentrism, but polycentrism is a stable and successful structure for handling novelty and status when the associated and traditional journal structure, refereeing system, and so on, are free from too much corruption.²⁵ Although polycentric structure allows a variety of locations for success, it is important to realize that this is coupled with the fact that no single location is the determinant of scientific success. The various locations make proposals, and the pres­tigious locations have the best opportunity for success in the resulting process of valuation, but disciplinewide recognition comes from con­vincing a large number or a majority in the discipline that some the­ory is best, or that some experimental result is right.

Polycentrism allows research groups to intensify and proceed, and then make their appeal to scientists of widely different backgrounds and convictions. Provided communication is reliable, and success is recognition by others in open competition, the polycentric structure of science is stable and progressive. Now it is possible to imagine that the reward system might not be polycentric, that is, dependent on recognition by one’s peers. Financial and political rewards might be given to scientists by some bureaucracy, and this is compatible with high motivation and good science in the long run, provided that the relevant political authority has the astonishing ability to recognize good science and to bias the award system to reward only the best work. Given what we have said about scientific history, however, such abil­ity seems to be nothing more than a bureaucrat’s illusion. The nature of developing significance in science seems to require competition, and then reward, as the polycentric system of reward operates. An effort to take the waste out of the competition must require a concep­tion of methodology that allows one to calculate the future significance of scientific work in the present. Because of this, the threat to poly­centrism posed by the funding of big science has serious conse­quences for the dynamics of scientific progress.

To this point, we have looked at similarities between disciplines, subdisciplines, and research groups. We have found, tentatively, that all scientific disciplines can be analyzed into small research groups that have similar structural properties. When we look carefully at sub­disciplines within particular disciplines, some interesting additional structure can emerge. Chemistry, for example, can be divided into eight subdisciplines, between which there are differences in consen­sus, instrumentation, competition, size of research groups, secretive­ness, and so forth.²⁶ There is a tendency for subdisciplines emphasiz­ing theoretical work to be represented by small research groups, and subdisciplines emphasizing applicability to be represented by larger research groups. This fact does not seem surprising, since the instru­ment of theory is still frequently the pen or pencil, but the instru­ments of applied science are likely to require special personnel, and the results likely to benefit in significance from repetition and from a variety of viewpoints. A subdiscipline like organic chemistry uses a variety of spectrometers, instruments that do not require special per­sonnel. Spectrometers do not correlate to specific problems, since they can be used to characterize virtually all organic compounds. Or­ganic chemistry, therefore, frequently exhibits small group or even individual research. In such an area, an individual scientist (with re­search assistants) may do a lot of experiments, publish many papers compared to a theorist, but produce work that is not widely cited directly by others, since it will be picked up into data compilations if it is of high quality. A theorist will publish fewer but more widely cited papers if he or she does good work, and a biochemist may work on more varied topics within larger research groups. This suffices to introduce the concept that research group size and style may depend on a wide variety of cognitive and experimental factors. We may ex­pect to find correlates to these differences in chemistry in the subdis­ciplines of other scientific fields, so that while such research may tell us something about research within subdisciplines, it will not reveal much about differences between disciplines.

Having failed to find interesting differences between scientific dis­ciplines in an analysis of the social structure of research groups or subdisciplines, we can return to intuitions about the differences in the disciplines as one moves from physics to sociology along the se­quence of traditional disciplines. Many of them, of course, fail of dem­onstration. As we have noted, citation analysis found no differences in the temporal pattern of citations in physics and sociology although the intuition that there has been greater progress in physics seemed to suggest that physics citations would, on average, refer to more recent literature than sociology citations. As we move from physics to sociology, the number of normally recognized subdisciplines or re­search topics seems at first to increase (chemistry and biomedicine) and then to decrease again.²⁷ Even when the number of scientists in the disciplines is considered, this fact seems to say little about con­sensus or progress in these fields. There is a tendency for group work to become less frequent as one moves from physics to sociology, but the factor of instrumentation makes it clear that the existence of group research can be quite independent of considerations of consensus or progress. In other words, particle physics experimentation requires group effort to operate the relevant equipment, but sociologists can run surveys by themselves and analyze the results on a computer. Instrumentation may also explain why the cost of research per scien­tist declines steadily from physicists to sociologists. Computer use is now common to all fields, but beyond this, instruments differ. Phys­icists use enormously expensive instruments, and in many cases highly specialized instruments, while sociologists use survey techniques and statistical models that are common to most sociology subdisciplines and do not depend on specialized instruments. In publishing, there is a tendency for physicists to publish more letters and articles than books, and for sociologists to publish somewhat fewer articles and more books.²⁸ It could be thought that this indicates greater consen­sus in physics, since the article may presuppose more, but this is hardly an obvious conclusion. Articles are designed for other special­ists in research groups oriented to similar topics. In physics (and mathematics) an attempt to go outside the research group runs into the problem that the special languages of research in physics are not immediately intelligible to other researchers. Articles are written be­cause only other specialists are the intended audience, and they can understand the article format because of shared expectations. In so­ciology, there are no specialized languages of research, at least none that can’t be explained relatively quickly in an ordinary language. There is thus the permanent temptation to argue the significance of specialized research results with a wider audience. The small amount of time that must be invested to do this may pay great dividends in disciplinewide recognition, while the time investment in physics would be substantially higher, partly because of other research that must be mastered to advance a large thesis, and this time investment would a fortiori tend to cause the author to fall behind that state of research in his or her home discipline.

The difference between the division of labor in physics and sociol­ogy, for example, seems intuitively real, and deserves further study. In physics, research projects oriented toward some goal can be broken up in many cases into smaller problems, with research physicists sep­arating into groups attacking these problems. Specificity of problems means that communication with those working on other problems is made difficult by shared assumptions that may be difficult to articu­late, but where the division can be justified it can be assumed that a good solution to a subproblem will contribute to a solution to the larger problem.²⁹ A trained physicist learns to convert his learned skills into instruments for attack on the specific problem that is the focus of his research group. By contrast, research problems in bio­medicine or sociology are likely to be oriented toward projects that are not so divisible, and with respect to which a solution to a sub­problem may cause great hazard for the possibility of solving another subproblem. Lowering the death rate in one area may raise it alarm­ingly somewhere else just through the technique that caused it to be lowered in a special case in the first place. Biomedicine and sociology seem to deal with systems that are not so easily broken into inde­pendent subsystems. Thus researchers may tend to bring existing ex­pertise to bear on the problems involved, and may feel more of a necessity to communicate with others working on the same problem in order to avoid overlooking consequences of their own line of think­ing. While these differences may tend to appear, and while typical physics research projects may be differentiated from typical sociology research projects using structural properties related to these differ­ences, it seems unlikely that physics and sociology can differ uni­formly in this way. Physicists can study systems, and sociologists have some divisible problems. Research strategies are therefore unlikely to be specific to disciplines, although there may be tendencies for dis­ciplines to be associated with research projects utilizing recognized strategies.

Differences between physics and sociology can perhaps better be traced to differences in the way in which their problems arise and to differences in the way in which their theoretical vocabularies take on significance. For sociology, significance in theory is generally related to significance that has already been determined by everyday expe­rience. Sociological theory, by comparison to physical theory, uses explanatory variables that have relevance to everyday life, for exam-

pie, income, profession, age, sex, status, religion, race, residence (ru­ral or urban), political attitude, and social class.³⁰ Social class is clearly the most theoretical term here, and this qiay be why the notion has been resisted by empirical sociologists. Some Marxists and various other social theorists have suggested that the failure of empirical so­ciology to develop theory like that of physics results from a concen­tration on the ideological veil of society as it is given in ordinary language, a concentration on concepts that deliberately mystify the actual structure of a society. This critique, while in many ways cogent, doesn’t seem to go directly to an even deeper problem.

Physics deals with the constituents of very small systems up to larger molecules, and in its experimentation it is free to handle large aggre­gates of theoretically identical objects of scientific interest (for exam­ple, electrons) that can be prepared for experimentation and brought into a (theoretically) identical state. When human beings are objects of consideration, as in psychology and sociology, it is clear from the­oretical biology that there is a problem.³¹ Any pair of human beings will almost certainly differ genetically, and if not genetically, they will theoretically differ because of differing past experiences. Any two hu­man beings thus have the theoretical potential to behave differently in any circumstances where their biochemical or cognitive capacities may make a difference. In physics, experiments can be replicated, bugs ironed out, and experimental results tied down definitively. Two physicists can know that their similar instruments should interact with interchangeable experimental populations in the same way. Experi­ments may be repeated on theoretically identical populations. A phys­icist may therefore freely project from one experimental population to all similar populations, and he or she may regard the experimental population as a fair sample from a much larger population that is well defined. This has considerable methodological impact in justifying various inductive policies and rational expectations. The experimental situation in physics underlies a well-defined division of labor. The theorist may know that the data of the experimentalist are exactly what the theorist would have obtained if the theorist had experi­mented in the same way. The theorist is therefore free to theorize without worrying about the legitimacy of the data used to constrain his or her theoretical development. In physics, so to speak, the ex­periments are the fixed points, and theorizing is the luxury permitted to physicists with respect to their data. A physicist obtaining data at odds with previous experiment, or at odds with legitimate theoretical extrapolation from previous experiment, will be cautious. Sources of error will be canvassed, and the experiment redone. The risk of pub­lishing variant data is that someone else may do a better experiment, exposing the source of error and diminishing the reputation of the overly hasty scientist. In sociology, theories are treated as fixed points, at least in the sense that they can be understood without the relevant experimental data. A sociological survey of college freshmen in Cali­fornia produces a certain result. If another sociologist gets different results in a survey of sophomores in Illinois, the researcher is free to publish without the same worries. The second survey is just as good as the first and may be just as reliable, since there are many relevant differences that might explain why two populations would react dif­ferently. Further, the interaction of a sociologist with his or her sub­jects is subtle, and may influence the results, so in fact there can be only an initial presumption that the two experiments were the same. The sociological theorist is not therefore able to assume that personal experimentation would lead to the same experimental results re­ported by others in the literature, and for the reason noted, a socio­logical experiment can never be exactly duplicated, a source of du­biety for the theorist.³² A sociologist with variant results may rush into publication without the same level of anxiety of a physicist. So­ciology thus tends to produce a pattern in which the lack of control possibilities for determining repetition and differing theoretical ex­pectations is associated with the accumulation of divergent and even contradictory results, which can be weighted quite differently by dif­ferent investigators, while physics seems to orient toward eventual consensus and truth, because its partial texts are more easily woven into a consistent whole by repetition and repair.

If one wishes to retain the intuition that physics and sociology dif­fer, it seems misguided to look for this difference in terms of the social structure of the disciplines or the research groups. The difference also seems to elude the invocation of paradigms, or feelings about the relative intelligence of the scientists in the two fields. Physics differs from sociology because of substantive differences in their subject mat­ter and in the instrumentation that can consequently be used in ex­perimentation, and because understanding enters the dialectic of the­ory and experimentation at a different point in the two sciences. Neither human free will nor human unpredictability is required to mark out this difference. The Appendix will take up this point in order to sur­vey more systematically differences said to exist between the natural sciences and the human sciences, in spite of their sharing of the basic scientific dialectic of theory and fact. At this point, the relevant con­sequence of the preceding discussion is that there is no feature of the social structure of different scientific disciplines indicating that they produce substantively different kinds of knowledge, or that the knowl­edge produced by some scientific disciplines is more objective than that produced by others. All of this tends to obscure any suggestion that there is an unequivocal basis for making judgments about the relative rate of progress in different areas of science. Rates of progress must be traced to the availability of appropriate data domains.

Controversy and Progress in Science

If the long years of training of scientists resulted in the absorption of the norms of scientific practice so that a scientific habitude resulted, as Kuhn has suggested, there would be no cognitive reason for con­troversy in science. Similarly, if scientific knowledge could be grounded in observation, as in the empiricist and rationalist traditions, there would again be no cognitive reason for controversy. For any of these views, prior acceptance of authority would suggest that the counsel of reason would be to pursue cooperative further investigation. Because of the presuppositions of both sociological description and philosoph­ical epistemology, controversy has always seemed to define some hu­man limitation in the practice of science. Controversy between sci­entists is to be construed on these models as an eruption of human emotion over human reason, or as an eruption of a personal desire for scientific recognition based on some psychological imbalance. Because scientists are human, it might be argued, controversy must enter into scientific advance. One partial exception to this view is represented by Popper, who sees competition among ideas as analogous to biolog­ical adaptation, with the survival of the fittest ideas a desirable con­sequence of competition among them.³³ Since Popper makes a place for criticism in the competition of ideas, it may be desirable here to distinguish controversy from mutual criticism or even intense debate. It is genuine controversy, emotions included, that will be the focus of our immediate concern. Nearly every extant view considers contro­versy, over and above debate and criticism, a mar on the rationality of scientific behavior. And yet controversy persists in science.³⁴ If science is to be even partly differentiated from nonscience as a bearer of rationality and objectivity, it would seem interesting to discover that controversy is not a mere blot on scientific history.

Although there are controversies in science, it is also characteristic of at least some scientific controversies that they get settled, at least provisionally and for lengthy periods of time. The controversy be­tween steady-state cosmologists and other cosmologists, quite heated for a length of time, resulted in the capitulation of the steady-state theorists. Adverse evidence took its expected toll, and it is easy to point to a variety of occasions in scientific history when controversy has been more or less ended by adverse evidence. By contrast, phil­osophical and religious controversies have stretched over centuries without attaining a clear terminus. It has already been indicated that controversy in science is not rational after sufficient text from reality has been produced so that only one plausible interpretation of it is known. Because text can be generated, the possibility of settling sci­entific controversy always exists, at least in principle, even if the tech­niques for producing crucial text are not always known in the early stages of controversy. But this returns our thought to its previous resting point. If controversy can be resolved by the production of text, why should more than cooperative criticism and mutual investigation exist in science if it were not for irrational factors?

One way to find a common thread in the irrationality of contro­versy—a way to make it rational, so to speak—is to shift consideration of scientific controversy from a cognitive plane to one of social inter­ests. Bourdieu has provided a brilliant sketch of how this may be done if we regard scientists, not as pursuing truth, but as pursuing scientific authority, the scientist’s socially recognized capacity to speak and act legitimately in scientific matters.³⁵ On this model, a certain amount of scientific capital is to be shared by scientists, who are then engaged in a partly political power struggle to maximize their share. In this struggle, recognition must be won from one’s peers, but such recog­nition is never given for merely cognitive reasons. Successful maneu­vering in this struggle is a function of origins, schooling, choice of field, strategy of attack on problems in the field, and so on, and not simply a function of intelligence and the quality of one’s work. Indeed the quality of work is not a fixed datum; rather, it is something that one must struggle to achieve by establishing that it is more worthy of recognition than the work offered to the community of specialists by one’s rivals. As in all political struggles, there are relatively risk-free rewards to be obtained by good party members, and there are risky but great rewards potentially available to those who subvert the pres­ent party and replace it with a new alliance. Clearly scientists choose careers and strategies within careers, depending on their assessment of their accrued scientific authority and on an estimate of their best means of investing that authority in order to maintain it or even to augment it. That science is not a purely disinterested quest for truth is shown by the anxiety surrounding anticipation of one’s work by others, some of the controversy in science must be the result of the attempt by scientists to amass scientific capital, but only a small step along this path of analysis seems to threaten any hope of locating a sufficient cognitive component to allow room for objectivity in sci­ence, or for any other than an instrumental rationality in scientific practice. It would once again be inconsistent with the variety of sci­entific practice to assume that all scientists have had the career am­bitions of pirates.

An attempt to see both cognitive and social aspects in controversy can be traced to the undoubtedly correct assumption that each indi­vidual scientist will have his or her own cognitive system. Any new piece of information must consequently be fit into as many diverse cognitive structures as there are scientists who find it interesting, but the significance of this information will vary widely with the cognitive structures into which the information must be assimilated.³⁶ To con­sider a crude polarity, new experimental data may be assimilated un­changed into the cognitive systems of many experimentalists, but be assimilated merely as support or denial of more abstract information into the cognitive systems of theorists, who will accept that the data do or do not fit theoretical parameters, with tolerance being granted to experimental error. If scientists are highly intelligent, and if they are highly trained, it seems inevitable that they will possess highly individualized outlooks. A contrary assumption based on acculturation must considerably overestimate the effectiveness of teaching in the learning process. Textbooks written by different authors always pres­ent theory slightly differently, finding a slightly different center for basic understanding of the theory, and emphasizing slightly different consequences of the theory as its most revealing aspect. Bellone has argued that each theorist must translate data into theory using a pri­vate dictionary, and that each experimentalist must translate theory into experimental design using a private dictionary.³⁷ Diverse diction­aries will contain slightly divergent pieces of mathematical and sci­entific information, but these pieces of information will be weighed differently in the dictionaries according to philosophical presupposi­tions. Because the dictionaries contain philosophical weightings that may be influenced by, or expressive of, social, religious, aesthetic, or political opinions, Bellone argues that attempts to separate internal and external history must fail. This picture is surely correct, but it threatens once again to divide the history of science into individual biographies that are difficult to bring into a meaningful historical pat­tern. What must in the end unite different theorists into consideration of the same theory is an orientation toward a certain range of data gathered in certain ways, and a recognition that the data constrain scientific thought along certain lines. The individuality of scientists explains why theories cannot be easily falsified by counterexamples, eliminated by data, or completely devastated by revolution. While a majority may revise their dictionaries drastically in the face of con­trary evidence or the piling up of anomalies, some will work at con­servative revisions, thus maintaining a wide potential variety of ideas in the gene pool of scientific adaptation to data. This point will take on increasing significance below. If the individuality of scientists ex­plains why scientists might engage in controversy, particularly in a setting where the accumulation of scientific authority is at stake, it does not yet provide reasons for considering controversy to be a sound cognitive norm, although it may be taken to reveal why controversy will exist in all disciplines, independently of sociological measures of relative theoretical consensus.

If methodology could actually play the role postulated for it by many philosophers, then a scientist following correct methodology could be assured that the resulting piece of scientific information would have to fit somewhere into scientific explanation. Scientists could be re­garded as fitting together a giant jigsaw puzzle whose pieces were produced in accord with sound methodological directives. A pervasive theme of this discussion is that methodology in the relevant sense does not exist. When a new piece of scientific information is offered, it is not at first known whether it is a piece to be fit into the jigsaw puzzle or not, no matter by whom it is proposed or how it is obtained. In subsequent discussion, this view will be set into a conception of scientific history and a conception of scientific fact that seem required to make sense of extant scientific practice. For the moment, it will be assumed that it is possible that the significance of bits of scientific evidence is not necessarily given to inspection. Under these circum­stances, why shouldn’t the self-doubt of scientists be converted into an even belligerent defense of the significance of one’s work? Such a psychological mechanism is readily imputed elsewhere, but it has been neglected in the study of science, perhaps because the imputation of rationality and objectivity to science makes one forget that the ulti­mate status of new information there may not be different from the status of new information elsewhere. The scientist wants recognition that his or her discovery belongs to scientific history; thus the tend­ency to defend one’s own claim takes precedence over the tendency to attack another’s claim as unscientific. Should attack prove success­ful, it would still remain open whether the defended piece of infor­mation was genuinely scientific. What is being suggested here is that the open significance of new information provides a cognitive role for controversy. Controversy is one aspect of the struggle to establish that some new piece of scientific information is significant, that is, that it deserves to play a role in the thinking of other scientists engaged with the same problems.

It would be wrong in terms of the norms of public debate to simply assert one’s opinion that some rival piece of scientific information was not significant. One problem is that at any given time in scientific history, apparently contradictory pieces of information may all be judged significant, the hope being that a novel way of fitting these pieces together can be found, or that they can be reinterpreted as noncon­tradictory in a new theoretical setting, as happened with the pieces of information put together into the quantum theory. The first cog­nitive priority is thus defense of one’s own contributions. Other con­tributions can be attacked as self-destructing or careless. A contribu­tion is self-destructing if it entails consequences at odds with its own assumptions and presuppositions. It is careless if it is not rigorous, either in logical development or in failing to note properties of exper­imental setups that are known.to be relevant. Failure of an experi­ment to replicate shows carelessness of the latter sort may be in­volved. Where these strategies cannot be exploited, simply ignoring apparently rival claims may thus be an effective, energy-saving method of dealing with them that is consistent with the norms of public de­bate. This is a hostile indifference, and part of controversy. It is not unknown in science to have research areas fragmented into research groups that exercise only incestuous citation, simply failing to ac­knowledge rival work whose existence is all too well known.

If controversy plays a cognitive role in settling the significance of new work, what prevents controversy from destroying science, and from eating up the time that could be spent on other forms of pro­ductive practice? The contrary tendency is differentiation of interests and research goals. Differentiation can be used to avoid outright com­petition and its associated controversy. As scientific text is elaborated, it raises new problems, new questions, and new issues of interpreta­tion. Rather than run the risk of losing in the competitive struggle to obtain some recognized desideratum, scientists may choose to engage a fresh topic where the chances of anticipation are minimized. Com­petition can be intense where there is consensus on important prob­lems and there are widely accepted skills and instruments for working on the problem.³⁸ Rather than be crushed in such a race, some may prefer to choose a somewhat more private goal. Gilbert, investigating radar meteor research in England from 1945 to 1960, discovered more topics for investigation of researchers, and he also noted that the dis­tribution of researchers across topics implied that researchers were not afraid of being anticipated in their current research.³⁹ At the same time, none of these lines of research was likely to cause a fundamental change in theory, or to promote wide scientific recognition for its successful completion. If scientists seeking a large increase in scien­tific authority may collide in the rush to establish priority in the so­lution of what are recognized to be important questions, in other areas of advance matters are more peaceful. Scientists can divide work am­icably enough when more modest shares of capital are involved.

Controversy and differentiation can play cognitive roles in estab­lishing the significance of new information and in finding new topics for research in the setting of an institutionalized science in which routes of scientific communication are well established. Because of this, what has been said here about controversy and differentiation is true of established nineteenth- and twentieth-century sciences, but re­quires modification for nascent science as well as science in the sev­enteenth and eighteenth centuries. There is no doubt that modern science began with a revolution in the course of which nature (as opposed to man) was secularized and became dead to man, that is, became an object for dispassionate scientific study. At one point, the implications of science for a world view were discussed at all social and intellectual levels, in church sermons, and so forth.⁴⁰ Before long, physics and astronomy had become autonomous from surrounding so­ciety. Later, biology passed through such a period in connection with evolutionary theory before it became autonomous. The universe of science is a bundle of laws and connections there to be exploited by man. Statements about quasars, plasma, and superconductivity do not excite public debate. Even nuclear technology and recombinant DNA research, although issues of public concern, do not seem to threaten a change in world view so much as termination of the world, period. The technical issues require the injection of expert testimony, contra­dictory as it is. Revolutions in thought seem possible when new sci­entific fields are carved out, and they have occurred in the past as the process of establishing scientific disciplines has taken place. But once a field is carved out, it becomes autonomous or nearly so, and discus­sion of the sort that can influence expert opinion in the field becomes a matter of expertise. Ties to the general intellectual culture of sur­rounding society are lost.

We will consider, for our purposes, only the autonomous research groups of contemporary science. Given what has been said about con­troversy and differentiation within such groups, it is clear that the chance of communicating with others and winning recognition is de­pendent on advancing information that is easily intelligible and readily assimilated. This fact encourages small steps, the sort that fit into an existing pattern of thought, and hence can be scrutinized from the many perspectives of other researchers. Further, the high cost of en­try into modern research in terms of schooling means that while in­dividualized outlook will be the rule, there will be a background of acquired scientific plausibility whose transgression means that work will be ignored or simply labeled as nonscience. The sum and sub­stance of this observation is that revolutions in the intuitive sense of the word are probably nearly impossible in established sciences. Small steps and differentiation of existing specialty will be the rule. For this process, mathematics and formalization are helpful, since they allow comparison of the differences of theoretical frameworks similar enough to be brought into mathematical or logical comparison. Revolutionary activity, or genuine attempts to subvert the existing outlook, would have to depend on the expenditure of a good deal of amassed scientific authority if they are to have a chance. Bohm’s attempt to challenge quantum orthodoxy is interesting in this connection. Without his prior reputation, his attempt probably wouldn’t have been discussed by other scientists, and it is interesting how a presumed proof by von Neumann that hidden variable interpretations were impossible was used by many physicists to lay Bohm’s efforts to one side without discussion.⁴¹ Genuine revolutions must be rare in the research groups of modern science.

In spite of the abstract arguments against the occurrence of revo­lution in mature science, Kuhn’s influence seems to have led to the search for revolutions in science. The theory of plate tectonics can be described as a revolution in geology, or one might speak of the Keynesian revolution in economics. There are periods in which the sciences—indeed all intellectual endeavors—undergo rapid changes in outlook. At any given time, some disciplines will seem to undergo more rapid changes than others. Physics in the twentieth century, for example, seems to have undergone some rapid changes early on, and then economics, and then later biology and linguistics underwent rapid changes while physics seemed rather to be mapping out consequences of its earlier upheaval. Relative growth may seem like revolution, and if history is written in the right time scale, a rapid series of small steps from one point to another may be viewed retrospectively as a sudden jump from one point to another. In order to bring talk of revolutions into consonance with the abstract arguments that seem to favor small-scale changes, it is possible to argue that what are consid­ered revolutions in established sciences are typically historical arti­facts. An established body of techniques, instruments, theories, and data suddenly takes on a new significance and permits new linkages because of a seemingly modest new piece of information or a new theoretical outlook. This can be compared to the problem of specia­tion in Neo-Darwinian theory. If all viable current change consists of small mutations in existing matter that are modest enough to be com­patible with interbreeding, one still has to deal with the existence of quite diverse forms of life (on the assumption of development from a small amount of similar original material). The solution is to argue that environmental channels can steer lucky mutations into new niches where the colonizing forms can gradually establish permanence in isolation from the point of origin. When great men of science are studied in detail, it frequently turns out that teachers and acquaint­ances who did not establish scientific authority for themselves pro­vided a framework in which a small change led to an important dif­ference. As history is generally written without this detail, it may seem that the great scientist accomplished much more than was ac­tually possible.

The difference between history, in which revolutions occur, and research, in which they must be infrequent at best, can be seen in a microcosm in the research report. Since the research report is a cul­tural product designed to play a role in the struggle for authority and to advance the claim of cognitive significance for the author’s work, it does not pretend to capture the historical sequence of events. Authors of research papers may simply announce for this purpose that they had such and such a bright idea, and then go on to details of experi­ment that corroborated that idea. It is not necessary for them to spec­ify the concatenation of odd factors, such as the availability of certain equipment, a chance remark of a friend, and an error, all of which may have played a role in the origin of the idea; nor need authors even be aware of these factors. Nonetheless, a study of such instances has frequently revealed that the bold step or bright idea involved such a concatenation.⁴² Wittgenstein prefaced his Philosophical Investiga­tions with a remark by Nestroy that progress always seems greater than it is.⁴³ No doubt scientists who have grappled for a long period of time with some problem will see a sudden advance as more revo­lutionary than it will be seen by historians who wish to fill in the relevant context. Nothing is here intended to impugn the intelligence that provides steps forward. What it may be important to establish for understanding science is that all steps must be small enough to in­volve backbreeding into accepted ideas, so that no truly revolutionary steps can occur, just a series of quick, small changes. What we have is an evolutionary development in which some steps seem more pro­ductive than others, and may be given the title revolutionary to dis­tinguish this fact.

The history of science can be viewed as a search problem. Scientists look for observational text and theoretical text that will give mutual significance. Very simple observations about search may illuminate the scientific model. Let us consider a baby lost in some woods by careless parents. A search for the baby will proceed rationally if the area to be searched is divided up among the searchers. If there is varied terrain, it might seem rational to have swimmers search along river banks, and to have climbers comb any existent cliffs. As the search team increases in number, the areas to be searched can be subdivided. Although no mathematical theorems are relevant, it would clearly not be optimal for everyone to look at the same location. Sup­pose the baby is found. The reward, if any, goes only to the successful searcher, but the successful searcher could perhaps not have found the baby except for the division of search and the activity of the other searchers. Scientific research, though not coordinated from above as the baby search may be, also might not be successful except for the activity of all the scientists involved. The successful scientist searches an area not covered by the others, and his or her search of this area might not have occurred save for knowledge of what others were doing. Research has to be seen as a cooperative activity in which not all acquire fame, but in which the activities of all researchers may play a valuable role. Just as the difference between the successful searcher and the unsuccessful searcher may not be anything intrinsic to their search methods, but a matter of looking in the right (or lucky) place, so the difference between the successful and unsuccessful scientist may lie, not in the embodiment of different methodologies, but in the matter of looking in the right place or having tried the right combi­nation. This is the social dimension of scientific knowledge that epis­temology cannot capture without an associated social theory. Episte­mology leaves the dynamics of progress untouched. We will develop a social theory of science further in the next chapter.

We can vary the search metaphor to yield an additional insight of some importance. Suppose an unknown territory is to be searched and mapped for annexation by a government. A preliminary search might best be undertaken by scouts, rather bold and rugged individ­uals who can rapidly canvass the territory, look for prominent fea­tures, and bring back information of considerable helpfulness to the more reserved map makers who must painstakingly survey the terri­tory and bring it within the confines of cartographic representation. Perhaps it is not surprising that we find different kinds of scientists playing a role in scientific history. Their joint efforts may be required for success, and yet they may have difficulty in understanding one another. At one time, improving a success rate from 1 percent to 3 percent in some experimental setup may be the important way to advance understanding, and this may require a scientist whose major skills are mechanical and manipulative. At another time, some bold extrapolation to possible new data by theoretical conjecture may be required. It is generally recognized that physics contains experimen­talists and theorists, two quite diverse roles, and analogues can be found in other scientific fields. If it be conceded that diversity of scientific personality and style can be a major contributor to the over­all success of scientific research, then we have located another aspect of scientific social structure that eludes epistemology, and because the roles are not labeled by the participants in every case and may be switched during investigation by the same scientist, this aspect must also elude any merely descriptive sociology. A last word on contro­versy and differentiation may be that they encourage this important diversity under circumstances where otherwise the maintenance of a gene pool of alternative but valuable scientific ideas would be swamped by consensus.

An analogy between scientific progress and biological speciation has been introduced that will be of value in considering the vexed notion of scientific progress. In biological evolution, an unchanging environ­ment is adapted to by species that may differentiate and adapt to various niches in order to fill out the available biological space with a stable configuration and distribution of forms. A changing environ­ment will be met by genetic change in which various forms from the combinational possibilities will be tried for adaptive success in the new environment. This process will result in a new stabilization if the environment settles down once again. Is the history of biological spe­cies a history of progress, as opposed to mere change? Species dis­appear, new species appear, and species may fluctuate widely in their numbers over time. The environment may also cycle, seeming to re­peat itself from time to time. It is the ability of species to produce different forms, to maintain genetic diversity, that allows them to change and adapt over time. Inflexible species will die out in cases of suffi­cient environmental change. Progress is an obscure notion here. What we have is a process that allows life to continue as the environment changes. An earlier form would not necessarily fit in the current en­vironment, nor a current form fit in an earlier environment. Rather than progress, we have continuance. Progress in a philosophically rigid sense can only be defined as a continual closure over time toward some goal. When one has one thousand tiles to clean, one makes progress as one cleans tiles, assuming that the cleaned tiles do not become so dirty again during the process of cleaning that they must be redone. An early candidate for the goal of science was a complete and accurate description of the universe. When this goal has been set aside, as it has been here, progress toward such a goal no longer can function as the measure of scientific progress.

More recently, the progress of science has been taken to be iden­tical with its ability to solve an increasing number of problems.⁴⁴ There are obvious problems with this proposal, even if it seems the only current possibility for avoiding relativism while acknowledging that no independent standard of ultimate truth is available for measuring epistemic progress. Even if science can solve more problems than ever before at each relevant point in time in its history, this need not be consonant with the intuitive notion of progress. Suppose, for ex­ample, that science throws up ten trivial problems each year for ten years, and also ten important problems, but solves only some of the trivial problems. One might not wish to say that science was progress­ing under these circumstances, especially if it had been solving im­portant problems, since the existence of science, and civilization, might be progressively endangered by the inability of science to solve its new serious problems. Problem-solving accounts of progress must inevitably run into the problem that it is hard to individuate problems and assess their relative significance in a manner that permits prob­lem-solving ability to measure progress. At the level of individual research programs, it is easily recognized that during any period of time, some of them will seem to be progressing toward their chosen short-term goals of research, others will seem stagnant, and others may seem to be retrogressing. Science as a whole, in all of its parts, is surely not continually progressing at all. A retrogressing or degen­erating program may suddenly reverse its direction because of a new idea or the discovery of new goals, but it may also continue to degen­erate. What we demonstrably have with modern science is simply continued life for three centuries, and the ability (so far) to adapt theoretically to experimental data. Many older scientific solutions to problems are no longer relevant, many simple theories have been replaced by complex theories over more recent data, and so forth. We cannot extrapolate from this past history of science to a successful future, project continued progress, whatever progress may mean.

If we view the paleontological record of a species, we may discover that it grew smaller in body size and then grew larger again, or that it lost and reacquired some measurable physical property. Viewed as a succession of forms, little can be said about why such changes oc­curred, only that they did occur. In order to understand and explain such changes, a knowledge of the environment is required. Perhaps the environment was cold, then hotter, then cold again, and a larger body size was more adaptive to the cold environment. Philosophers who have studied only the internal history of scientific theories are confronted with something analogous to the fossil record of forms without a corresponding record of the environment. In order to un­derstand the succession of theories, one must take into consideration the data base to which these theories were attempting adaptation. New data, for example, could change the problems to be solved and set a theory back until a new form of the theory designed to adapt to the new data was available. Underlying the history of theory is the history of data text. What is cumulative in the history of science is the gradual refinement of scientific instruments once they are intro­duced until they produce data that seem to be robust in the face of further refinement. For some instruments, for example, the micro­scope and telescope, no theoretical limits to such refinement seem imminent. But certain objects studied by these instruments have re­mained in the data base since their discovery, and information about them has been gradually made more precise. A changing data envi­ronment for scientific theories is like a changing environment for bi­ological species. Progress is not guaranteed, but theory contains adap­tive measures that allow it flexibility in the face of such change. Of course these remarks freeze the dialectical interplay of theory and experiment by making it seem that data are fixed for theoretical ad­aptation, but it is important to see that concentration on internal the­oretical change cannot by itself lead to any insight into progress, nor can concentration on the problems that such theories can solve. Rather than attempting to find a goal or property of science that assures prog­ress, we will concentrate on the mechanisms for theoretical adjust­ment to data that have allowed scientists to adapt theoretically to the data environments that their instruments have located. While not en­suring progress, this perspective will break with the evolutionary analogy, for the sequence of scientific instruments will allow us to find a direction in scientific research that mediates the pessimism consequent to the sheer evolutionary analogy.