II. WHAT IS A PROBLEM THAT WE MAY EVALUATE IT?
By Noretta Koertge
Introduction:
According to naive empiricism, scientific inquiry is driven by the need to organize observation reports in such a way that we may make predictions about future observations. What we seek to codify depends (internally) on where we can most easily elicit strong empirical generalizations and (externally) on which sorts of phenomena it would be most valuable to be able to predict.
According to a hypothetico-deductive account, hypotheses are put forward in the hopes of giving an explanation of, or, as some would say, an economical axiomatization of observable phenomena. The vocabulary in which the hypothesis is formulated may go well beyond the language in which we describe our observations and may introduce concepts quite foreign to our ordinary experience. Simple H-D methodology gives no account of where hypotheses come from (other than to relegate that question to the "context of discovery") and provides no internal story other than that of economy of thought about why hypotheses are entertained regarding some phenomena but not others. It is compatible with various external scenarios about why certain domains are thought to be in need of explanation at particular times.
From the beginning of his philosophical career, Popper has argued that induction was a description of neither the psychology of scientific investigation nor the logic of evidential support. Although his title Conjectures and Refutations is reminiscent of the H-D approach, Popper also talks a lot about the pre-conjecture stage of scientific inquiry. His slogan is "science begins, not with observations, but with problems". And if we are successful, the results of the scientific process are also problems, but the new problems are in some sense deeper than the old. The essays in Objective Knowledge make frequent use of a little flow chart:
P -> TS -> EE -> P' (Figure 1)
where P and P' stand for problems, TS for the tentative solution, and EE represents attempts to eliminate errors. Popper introduces this schema on at least ten different occasions in Objective Knowledge. He usually describes it as the method of trial and error and sometimes replaces TS with TT for tentative theory. In one place he says it is his alternative to Hegelian dialectic(p.297).
In this lecture I wish to fill in more details on the Popperian flow chart and then use it as a matrix for further discussion of questions relating to science and ideology, and science and society.
1. An Overview of Scientific Inquiry
I will now introduce an expanded version of the Popper schema which incorporates language of which he might not approve, such as "Research Program" (he especially disliked Lakatos' notion of "hard core") and "Context of Justification" (he would obviously prefer to talk about the context of criticism or severe testing), but I will use these more familiar terms in a rather vague, non-technical way that is not intended to prejudge issues about confirmation vs. corroboration nor to incorporate definite claims about exactly how metaphysical context influences research.
Figure 2 lays out the stages of scientific inquiry. It is completely non controversial to say that "external" social concerns both do and should dominate choices made within the Context of Application. And it is widely believed that social factors should not and usually do not play a significant role within the Context of Justification. We will reexamine these assumptions a little later but let us now focus on what I have labelled the Context of Discovery. The first question is a familiar old chestnut in science policy discussions: To what extent is it appropriate to let social concerns figure into decisions about what research should be carried out? I hope we can say something fresh on this subject. The second one is more tendentious and plays a key role within the so-called "Science Wars" discussions: To what extent should we let ideological considerations guide the range of the range of hypotheses we accept for testing? A guide to this controversy is provided in Figure 3.
2. An Internalist Typology of Scientific Problems
Beginning our account of scientific inquiry with problems instead of observations or axiomatic principles promises to allow us to make a philosophical study of what, following Reichenbach, is called the "context of discovery". Instead of leaving the process that generates hypotheses to the psychologist or historian we can analyze the types of problems that trigger scientific advances and comment on problem structure and the cognitive considerations that govern problem choice within the scientific community.
Popper introduces several varieties of scientific problem. He most frequently refers to problems arising from failed expectations. Part of our biological heritage is to form expectations about forthcoming events. When the pattern we either consciously or unconsciously anticipate does not occur we wonder about what happened and seek for an explanation of both the previous pattern and the new exceeptional event. A classic scientific example would be the "problem of the planets". In general, heavenly bodies appear to move in smooth arcs across the sky. However, the planets ("wanderers") exhibit retrograde motion. Can we give a unified account of both the regular motions of the sun, moon, and stars plus the irregular motions of the planets?
Popper also alludes to what I will call problems of deep explanation. Here one is faced with a perfectly serviceable empirical generalizaation but wonders what underlies that regularity. Why do objects always fall to the earth? Why is the sky blue? Why do mama rabbits have baby rabbits instead of baby frogs? Although this sort of explanatory curiosity about how things work is a deeply ingrained feature of human psychology, a salient feature of scientific inquiry is that scientists seem not to run around in all directions asking Why-questions. At certain moments asking why the sky is blue seems to be a suitable project for inquiry; at other times it would be laughed off - "it just is blue, that's all". (Contemporary examples might be questions about why all electrons have the same charge or why mass/energy is conserved. Most scientists today would not consider those to be fruitful research questions, although some at the cosmological fringe might find them interesting.)
This circumstance raises a philosophical problem: Can we give an account of what makes certain generalizations seem problematic and others not? (Where do explananda come from?) Hattiangadi has argued that all problems are rooted in inconsistencies. He would consider what I have called problems of deep explanation simply to be those special cases where the tension is between the tenets of a metaphysical research program and an empirical generalization. So, for example, what made the retrograde motion of the planets problematic was not so much that it was unexpected (after all the retrograde motion is periodic and predictable) but that it conflicted with the theory that the motions of the unchanging celestial bodies should be circular. The problem of the planets was not just to "save the phenomena" in any economical fashion. Rather it was to reduce their orbits to uniform circular motion. We need not pursue Hattiangadi's account further at this time. But it illustrates one way to solve the problem of why scientists select certain unanswered why questions as problematic and worthy of investigation: they choose cases that involve conflicts with the prevailing worldview.
Although Popper does not speak of the following problem type explicitly, it seems to figure prominently in the history of science: it comprises what I will call problems of unification. Can one give a unified account of celestial and terrestrial motions, of inorganic and organic chemical bonds, of animal learning and human learning? Here again we need an analysis of how scientists decide two previously disparate domains need to be brought together under a single theoretical rubric. (For example, why were color and sound considered to lie in "adjacent" domains which might be given a unified treatment but tastes and smells thought to be disjoint?)
It is useful to introduce one more type of problem although it may turn out to be a special case of violated expectations: these are what I will call problems of filling gaps. Mendeleev's Periodic Law produced a beautiful codification of the basic properties of the known elements but when the elements were arranged into a table there were three gaps. Since one knew what their properties should be chemists set out on a systematic search for the missing elements and the discoveries of gallium, scandium, and germanium were taken as marvelous confirmation of Mendeleev's theory. Much of what Kuhn called "normal science" is devoted to problems of filling in lacunae in the current paradigm. From a Popperian standpoint we should perhaps view these efforts as attempts to refute the theory but that is not really how scientists would describe their activities. If the missing elements had not turned up, no one would have thought the worse of Mendeleev's system; however,if one discovered elements which did not fit the Table, that would be taken as refutatory, or at least anomalous (as thr Rare Earths were).
A quick perusal of these rough descriptions of four problem types immediately reveals that each requires a specification of what Popper calls "background knowledge", a set of more or less explicit claims that are taken for granted in a given epistemic context - they are not themselves under critical scrutiny. The expectations that are violated often lie in the background; problems of deep explanation or unification presuppose not only articulated theories to be explained or unified but also background beliefs that problematize these particular generalizations or domains. Filling in the gaps also presupposes some sort of semi-articulated research program that we are setting out to instantiate, not refute.
The complex system we blithely label "background knowledge" typically also contains hints about the directions in which we might search out solutions to the above types of problems. In the case of filling in gaps, the foregrounded theoretical framework can give us explicit direction (cf. Lakatos' concept of the "positive heuristic" of a research program). The reasons we have for trying to unify two domains may also tell us what sort of unification to look for. And we ususally don't consider a generalization in need of deeper explanation without some sort of basis for speculation about what sorts of underlying mechansms might be involved. (Again this is usually provided by a metaphysical research program such as Cartesian metaphysics or Newtonian corpuscularianism.) Violated expectations may become problematic because of some practical application, but otherwise we may tend to shelve them or consider the violation an unexplained "glitch" unless background knowledge provides us with at least a vague idea about what might have produced the exception.
There is one more exceedingly important function of background knowledge; it sometimes allows us to obviate or dispose of questions by showing that they rest on a false presupposition. Thus today a question about whether or not phlogiston has negative weight would do worse than receive a zero preference ranking - it doesn't even arise. Likewise for problems about the design of perpetual motion machines or the causes of telekinesis. Of course, given the fallibility and incompleteness of background knowledge there can be controversial cases. Until recently research on acupuncture would have seemed to many to be completely wrong-headed because our best scientific theories said that it was not only an unconfirmed phenomenon but also physiologically untenable. An interesting current theoretical case concerns the so-called "Anthropic Principle". If we ask why the physical parameters of the universe seem to be fine-tuned in such a fashion that the evolution of intelligent life is possible (i.e., that we can exist) are we posing an illegitimate scientific problem? (Let us assume that one can indeed show that if the gravitational constant were a little bigger the universe would collapse or that if it were a little smaller planets would not form, etc. etc.) Does the fact that the implied teleology of the question conflicts with our present metaphysical repudiation of purposes in the physical world render the question obviated? A significant minority of religiously inclined physicists, such as Tippler and Barrow, think the question should be allowed to stand. And interestingly, a non-religiously motivated physicist, Lee Smolin, has recently proposed a Darwinian model of the evolution of the cosmos which is designed to explain the fine-tuning in a non-teleological fashion! So we should perhaps not be too quick to rule a question out of court as obviated although we may well advise our graduate students or non-tenured colleagues to choose another research topic.
3. An Internalist Account of the Choice of Scientific Problems
These remarks suggest that it would be fruitful to analyze more carefully the structure of the above types of problem situations, but at this point I want to turn instead to some preliminary remarks about the factors that influence scientists' choices of problems for scientific investigation. Let us begin with purely cognitive considerations. We will then expand the domain of relevant factors to include technological, economic and broader social implications.
Adopting a simple decision-theoretic approach, we begin by distinguishing two broad dimensions of rational choice of scientific problem. The first deals with value issues: how cognitively deep/important/interesting is the problem? (Later we will add considerations of social importance.) The second dimension concerns feasibility: how likely is it that the problem can be solved? Here again we can include questions of both cognitive and technical/economic/social resources.
Let us look briefly at the cluster of factors which contribute to the cognitive value of a problem. When a problem arises from an inconsistency within the scientific corpus, the problem is more pressing the "deeper" the inconsistency. It is difficult to explicate the concept of "depth" but certainly one indication of a deep inconsistency is the content of the two clashing fragments. For example, when we have a contradiction between our best physics and our best astronomy (the situation facing Galileo) or between electromagnetic theory and the theory of atomic spectra (the situation facing Bohr), the problem is deep in the sense that regardless of which "pole" of the contradictories we decide to revise, the effect on our overall scientific corpus will be extensive. Such problems always rank high in importance although they may rank rather low as far as tractability is concerned.
Other problems are seen as important because of the content they promise to add to our system (Bromberger speaks of "value-adders'). Any theory which successfully unifies two disparate domains is bound to be "deep" not only in the sense that it describes underlying causes or invariants but also because the unifying theory will have to have at least as much content as the two domains and typically has lots of new implications. But even filling-in-the-gaps research can add a significant amount of content. Each new element lets us go on to explore its descriptive chemistry and leads to the synthesis of literally dozens of new compounds. And of course the search for a novel effect, such as superconductivity, has an even greater potential for adding both information and feasible new questions to science.
But there are more ephemeral sources of cognitive value, some of which seem less objective in nature. There is no doubt that scientists are also attracted by the sheer "puzzle value" of certain problems. Scientists, and especially mathematicians and logicians, sometimes describe problems as being "pretty" or "intriguing" or "deep" in circumstances where they seem not to be thinking about the content or centrality of the problem. Rather they seem to be referring to more aesthetic considerations. An example might be a problem that can be simply stated and appears as if there should also be a simple solution, yet turns out on examination to be extremely complex. Such questions are often also deep in the content sense but it's not obvious that the latter is their main attraction to theoretical scientists. We see that even before turning to social appraisals, the evaluation of just the internal cognitive importance of problems is quite complicated.
Even more difficult to analyze are judgments about cognitive feasibility. Perhaps it is best to proceed by analogy to the more straightforward concept of technological feasibility. In the latter case one is thinking primarily of the availability of instruments (including in some cases computational or statistical capability). Sometimes one must also consider whether the required pool of skilled personnel is at hand. But even prior to these practical questions is the more inchoate issue of whether the problem is, as scientists say, intellectually "ripe" for solution. Often, especially in retrospect, we can say that a certain theorem could not have been proved until a certain lemma became available. To study the causes of optical activity (the ability of some solutions to rotate polarized light) required not just a polarimeter but also a theory of the geometrical structure of molecules.
So far we have alluded to cognitive defecits, i.e. to factors that lead us to believe that a project is not feasible. However, there are also cases where we have positive reasons to believe that a problem is solvable. The most obvious instances are cases of fill-in-the-gaps problems where a theory or research program strongly suggests not only that there is an answer but may also dictate a heuristic strategy for searching for the answer. Lakatos describes some of the heuristic devices of Newtonian mechanics. As a first approximation, use mass points for extended bodies. If you need to postulate a new force, assume it is a central force. The General Correspondence Principle, discussed by Krajewski and Post, offers a heuristic guide for those who would explain violated expectations or try to unify disparate phenomena - design a new theory such that the well-corroborated parts of the old system come out as special limiting cases.
Now that we have surveyed the utilities and probabilities that enter into an internalist account of rational problem choice (namely, the cognitive value of a problem and the liklihood of solving it), let us briefly explore whether these two components are independent or whether they might balance each other out instead. Here are two reasons for being concerned that they are inversely related. First, as far as pure puzzle value is concerned, we might wonder whether part of the perceived value of a problem is its difficulty. If this were the whole story, then we might worry that all problems would receive the same priority ranking - the more difficult problems would be judged most important; any soluble problem would be deemed unimportant, and thus all would receive the same composite rating! This can happen, I believe, but luckily there are almost always additional determinants of both value and feasibility.
A similar situation could arise if we were to accept Popper's measure of empirical content as the inverse of logical probability and then use the same probability measure to estimate how likely we are to solve a problem. In such a scenario, for example, the bigger the two domains that we wish to unify, the more important the problem would be, but also the more unlikely it would be that we would succeed. Again all unification problems would receive the same ranking. However, there is no good reason at all to assume that logical probability is the way to rank the solvability of various problems in a given historical context. (Many have argued that Popper's use of logical probability in his arguments against induction is also illegitimate.)
I conclude that although it may be difficult in practice actually to access the cognitive utilities and probabilities that we need to make rational problem choices, there is no difficulty in principle in doing so. Furthermore, the above schema is very useful in explaining many actual developments in the history of science. We expect scientists in general to prefer problems that are perceived as being both interesting and tractable. Some risk seekers will choose to work on deep problems even if they seem insoluble (they may believe that they have a unique insight into how to solve them); others will choose problems of more mundane interest that can be approached in a routine way. No one, according to this model, will work on cognitively uninteresting problems for which there is no obvious solution strategy.
4. External Evaluations of Problems
It is a commonplace to say that the direction of scientific research and often the rate of progress in that direction is strongly influenced by considerations of social utility. There are, of course, debates about the extent to which efforts to solve social problems benefit from a strong on going program of pure research, i.e., research that is guided solely by the cognitive utility of questions. Typically, scientists tout the indirect, unanticipated usefulness of cognitive problems while politicians want more research directed specifically at socially defined problems. Only scientists are really in a position to assess the solvability of problems; however,it is very tempting for them to gloss over the difficulties, in part because judgments about solvability are very fallible, but also because it is relatively easy to divert funds into the pure research they wanted to do in the first place while employing a rhetoric of social relevance. (Two anecdotes of such activities from my own experience: (1) A colleague who was applying for an NSF grant to study the history of medieval optics was advised to put on a title like "Early concepts of solar emanations" because at that time Congress was throwing money at projects studying non-fossil fuel energy sources. (2) A philosophy colleague interested in alternative logics, including relevance logic, was funded for some time by the Office of Naval Research because he was able to argue successfully that if Admirals used material implication their naval strategies would suffer. The development of relevance logic would improve military reasoning!)
Luckily, there are many research problems which rank high both as cognitively puzzling and as socially pressing. My conjecture is that one reason that AIDS research became so well-funded so quickly was not the result of AIDS activism or social compassion but because retroviruses were neat things to study from a purely biological point of view. Osteoporosis, on the other hand, although a quite significant source of human suffering, is a rather boring problem from the perspective of pure medical research - it looks unlikely to be amenable to a "magic bullet" solution. Given the possibility of serious conflicts in interest in appraising the importance/interest of scientific problems and given the fact that only scientists can make informed judgments about the cognitive and technical feasibility of solving problems at a given historical moment, it is no wonder that laypeople are often frustrated in their attempts to influence the direction of scientific inquiry. It is undoubtedly this circumstance that motivates many of the attacks on or attempts to effect radical transformations of science that we encountered in our discussion of the "Science Wars".
The examples of social utility that we have introduced so far have all gone to the goal of relieving pain and drudgery. There is a second sort of social utility that often overlaps strongly with cognitive interest but need not. I am thinking, for example, of the high degree of lay interest in the investigation of life on Mars, which could turn out to be of importance to our systematic understanding of evolution and the formation of the solar system but probably incites lay interests primarily because of its mythological connections. And although figuring out the life habits of dinosaurs is also of considerable intrinsic scientific interest, the creatures in the Burgess shale are probably of at least equal theoretical importance but will never capture the lay imagination in the same way, despite the best efforts of Stephen J. Gould. However, the more scientifically literate a society is, the more we can hope for an overlap in the appeal of problems to scientists and the wider community.
But although conflicts about awarding positive priority rankings to problems can be pretty bitter (American physicists are still smarting over the defunding of the Super Collider), the deepest divides occur when society argues that certain sorts of research questions must not be pursued at all. (See Figure 5.) The most common motivation for prohibition of certain lines of inquiry is a concern about dangerous applications of that kind of knowledge. The U.S.A. is presently considering a ban on certain types of human cloning research because of fears about how such a capability might be used. Some oppose research on genetic markers for diseases for fear that such information would be used by health insurance companies to deny coverage or by parents to abort fetuses. The immediate internalist scientific response to such worries is to call for better regulation in the context of application and to point out that there are also possible positive utilizations of this "dangerous" knowledge. (I might point out in passing that this debate is as old as science itself. When Tartaglia, a predecessor to Galileo, discovered the angle at which to aim a cannon in order to maximize its horizontal trajectory he burnt his research notebooks because he felt that this knowledge was too dangerous to deseminate to his bellicose countrymen. Later, however, when the Turks were at the gates of Vienna, he published his results in order to save the "civilized" world.) Here again an uneducated public is at the mercy of scientists' judgments about possible good consequences. And scientists are also more likely to be impressed with any intrinsic cognitive appeal the problem may have.
Recently, the motivation for censoring or strongly discouraging certain lines of research has arisen from a fear that certain kinds of scientific results can be dangerous if they become widely believed even if they are never applied! At least this is the way I interpret some of the objections that are made to human sociobiology and research on gender, racial, or ethnic differences. I find many of these criticisms confused. Sometimes the argument appears to be that such investigation is bound to reinforce social stereotypes (but of course it could undermine these stereotypes) and that we somehow know a priori that these stereotypes can have no empirical basis and so to even raise the scientific question is to give comfort to reactionary elements in our society. It is also assumed that if scientific evidence that reinforced the stereotype were to be forthcoming then the social result would be to lead to further discrimination, not remediation. So, for example, after bringing up a variety of bona fide methodological weaknesses in research on sex differences, Longino then tops off her critique as follows:
"The work of Ehrhardt et al. translates vaguely [my emphasis] into support for traditional roles - whether in implicitly permitting teachers to allow boys to get away with less self-discipline and greater physical expressiveness or to encourage girls to be quiet and more domestically oriented." (Longino, Science as Social Knowledge , Princeton, 1990, p. 166) But such results need not be "translated" that way at all! If we have a fair-skinned child we now know to be especially careful to use sun screen. We give our hyper-active children drugs, shy children public speaking lessons, and aggressive children impulse-control counselling. And in other contexts feminists have urged systematic "sensitivity training" for males, whites, the able-bodied, etc. In the contemporary ethos where we have enormous, expensive technologies for reshaping our bodies and psyches, it is silly to assume that any statistical biological differences between groups would automatically be "translated" into affirmation for damaging stereotypes!
I think there may also be a deeper, vaguer fear that goes something like this. I'll introduce it with an analogy. Suppose that you are happily married, happy with your kids, happy with your job, etc. but one day, in a fit of Socratic an-unexamined-life-is-not-worth-living curiosity coupled with a Cartesian evil-demon methodology, you set out to systematically doubt the faithfulness, trustworthiness, goodwill of your intimates. You deliberately proliferate paranoid speculations about how they are all conspiring against you. Being clever it is not to difficult to find some evidence for them. After a few days of playing this game you now weigh the paranoid interpretation against the more benevolent picture you started out with and now rationally conclude that no, they aren't all out to betray you. Nevertheless, the effects on your psyche of engaging in this process of systematic doubt leaves you a little less secure. Although a Popperian would tell us that once a hypothesis passes a severe test we should now think more highly of it, psychologically it just doesn't work that way for you, partly, perhaps, because in the realm of social science passing and failing tests is not a very straightforward process - and you still don't know what those people were whispering about before you entered the room and they suddenly stopped. In this case, it could be argued, just to raise the question is damaging, even when the result comes out positively from a political point of view!
Perhaps some people feel that raising a question about the possible validity of stereotypes would have the same lasting bad consequences. Note that this phenomenon only accrues in cases where we can maintain some level of existential scepticism about the proposition. The paranoid example cited above works for me but I would not feel similarly threatened by an inquiry into the possibility that I am always dreaming or that bread will poison me tomorrow. So, the argument would go, some topics in certain historical contexts are too hot to subject to inquiry, not just because any results might be misapplied but because to even raise the question is to shatter some sort of fragile social contract we have undertaken to proclaim stereotypes false and evil.
I certainly don't go along with this argument in general, but I would conclude that when we are totaling up the prospective costs and benefits of doing certain kinds of research, it is only fair to include this fear factor into the calculations, especially if the question is one that is difiicult to do conclusive research on and if neither the intellectual nor social benefits of knowing the answer are significant. On the other hand, I would not endorse bans on or picketing of such research because here the danger to the spirit of free inquiry is much greater than the sort of harm to a fragile social psyche that we might want to prevent.
5. Other Aspects of Scientific Inquiry Where Internal and External Values May Conflict
We have seen how the priorities of scientists and science policy makers may differ and how lay people may wish even to prohibit certain kinds of research. There is an uneasy mutual dependency here - scientists are almost always dependent on outside sources of funding, whether it come from government, business or a royal patron! Society, at large, however, has to depend (although they sometimes try not to do so) on the scientific community for judgments about what can and cannot be done and the kind of resources that are needed to tackle certain problems. Scientists, like any other applicants for funding, often spin their proposals in a self serving fashion. Science politicians, on the other hand, often set down ignorant and unrealistic guidelines for how research should be conducted.
But at least all parties agree that it is legitimate that both external and internal considerations are relevant to some extent to decisions about the choice of scientific problems. However, there are other phases in the scientific process where even that limited amount of agreement is hard come by. Let us briefly survey these contested sites by continuing along the flow chart in Figure 2.
Once a problem is on the agenda we must formulate one or more tentative solutions and test them. These activities would seem to lie squarely within the jurisdiction of the scientific community. It may be tolerable to have outsiders tell us which research problems they will fund but once we undertake the tasks then surely it is up to experts to solve them without ideological interference from the outside. But some of the new commentators on science, propose to do just that. For example, Longino argues first that scientists from different backgrounds will find different hypotheses plausible or worthy of pursuit. One might dispute how important such factors are, but certainly no harm is done by having a wider proliferation of problem-solving approaches. (She has in mind race, gender, class differences but others have described variations amongst scientists of different disciplinary backgrounds.) But then she goes on to propose that the hypotheses pursued may also be restricted by race/gender/class considerations:
"I am suggesting that a feminist scientific practice admits political considerations as relevant constraints on reasoning.....[I]f faced with a conflict between [political] commitments and a particular model of brain-behavior, we allow the political commitments to guide the choice (1990, pp. 191, 193).
Longino does not give detailed reasons for this extraordinary proposal. It is one thing to claim that sexism (or whatever) has artificially restricted the range of thinkable hypotheses; it is quite another to argue for the deliberate exclusion of theories. It may be tempting to try to redress the balance by introducing one's own progressive ideology into the context of pursuit but what justification could there be for excising otherwise perfectly respectable hypotheses from the debate just because they appear to be politically regressive? Perhaps one might try to argue that since it takes time and money to formulate and test hypotheses, one should begin by giving politically progressive approaches a run for their money. (If I have lost my wallet in the garden and really don't have any idea where, why not begin by looking in the daisy patch rather than plunging immediately into the middle of the rose bush?) But the analogy is misleading because it really hinges on a pragmatic feasibility factor not wish fullfillment. To make the analogy parallel we would need to posit that I refuse to look in the rose bush because I hate Gertrude Stein, not because thorns will make the search more time-consuming. When ideological blinding occurs it is always regretable. I find it even more threatening to the integrity of science to try to censor theories than to censor research questions. It's better to not raise a question than to introduce bias into the answers one will entertain to it. It should be noted, by the way, that many allegations about the pervasive influence of gender stereotypes in the past disappear under the scrutiny of historians who are not themselves committed to politically correct history.
The Context of Justification or experimental testing (Figure 4) has also become a contested site of late. One thinks immediately of the interventions of animal rights activists. Here there are interesting philosophical issues but the debate has now moved pretty much into the arena of governmental regulation, with scientists readily agreeing that some regulation is necessary although there are sharp differences about how much and how it should be carried through. More central to the methodology of science are the arguments of AIDS activists against having control groups at all when testing new treatments on the grounds that it is unethical to deny possibly beneficial treatment to the terminally ill. (Besides we already have a control group - the medical histories of those untreated patients who have already died of AIDS.) The U.S. Federal government, on the other hand, has mandated more control groups in certain cases, requiring that tests of new medical treatments should be run not only on both men and women but also on the usual affirmative action categories of African Americans, Aleutian Islanders, etc. Here there is only the slimmest pretense of a scientific or moral rationale for the set of new methodological strictures. It is simply motivated by a wish to seem responsive to the medical needs of various politically identified identity groups. However, the practical problems in getting enough participants in each of the cells to make such a study statistically significant is almost insurmountable. (For a discussion, see Satel, "Science by Quota".)
Conclusion:
In this essay I have tried to indicate the value of Popper's Problem solving schema for analyzing conflicts that figure prominently in the "Science Wars". Perhaps of more philosophical interest would be to pursue the usefulness of this approach for advancing internalist discussions of scientfic methodology. For example: In his recent book Critical Rationalism, David Miller tries to present a version of Popper's philosophy of science that is purged of even a "whiff of inductivism".
Miller first suggests that we should adopt an "open admissions policy" to the corpus of scientific knowledge with the only restriction being that any admitted claim should be falsifiable. Any statement that is falsified would get turfed out; until it is falsified, however, he seems to want to say that the claim, no matter how outlandish is on a par with even the best tested scientific theories. (To refer to the test record is one place where a whiff if inductivism might creep in.)
However, Miller also realizes that this policy would not permit us to distinguish between the green and grue emerald hypotheses. It would also allow one to populate the scientific corpus with testable, but uninteresting singular claims such as "NK will type 4 pages on Jan 1st, 2001", "NK will type 5 pages on that day", etc. So Miller hints that we might want to add an additional admission requirement, namely that the hypothesis have been proposed as a solution to a (scientific) problem. This is one way of disposing of the grue hypothesis. I am not terribly enthusiastic about this move, but if we wanted to follow Miller here we would obviously need to have an account of what makes a claim a solution to a problem. Another possible use for a problem-solving approach is in connection with the notorious problem of verisimilitude. We will address this issue next time.
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