Social empiricism and its potential:

for a fruitful cooperation between SSK and philosophy of science

Tetsuji Iseda

The sociology of scientific knowledge (SSK) has been attracting much attention over the past twenty years. However, there are not so many serious attempts to incorporate such works into epistemological arguments. The purpose of this paper is to inquire into the possibility of such cooperation between SSK and normative philosophy of science. I discuss three alternative views, i.e. socialized epistemology as an extension of naturalized epistemology, Steve Fuller's "social epistemology", and Miriam Solomon's "social empiricism." As the title of this paper shows, I think Solomon's view is more promising than the others.

1. Various trends in sociology of scientific knowledge

There are many different and sometimes opposing trends in SSK literature, even though they all agree that science is socially constructed. The differences become important when philosophers have to consider what kind of sociology to incorporate into their own works. Obviously I do not have space for a detailed review of different schools in SSK. I have to constrain myself to a general overview (my manuscript A in the reference discusses these different research programs in SSK more in details).

1-1. Two senses of 'social'

First of all, when sociologists say "science is a social activity," the word 'social' is used in two fairly different meanings by different sociologists. First, there are sociologists who argue that society, as a causal factor in scientific practice , constructs scientific knowledge. For example, society shapes each scientist's world view, motivation, etc. and these factors affect the choice between alternative hypotheses. I would like to refer to this view 'social causation.' On the other hand, other sociologists argue that the scientific community, as a small society with its own structure, norms and decision processes, creates scientific facts etc. as a result of consensus. This is the second meaning of the word 'social,' and I call it 'consensus formation.'

According to the first view, society appears as a causal factor to regulate and to guide scientists' activity. Bloor's "strong programme" ([1976] 1991) is a clear declaration of this position. A representative work in this field is Forman's study (1971, 1979) that the intellectual atmosphere of the Weimar culture influenced the anti-deterministic interpretation of quantum mechanics. Collins finds that judgements on personality of each other played an important role in the gravity wave debate (Collins 1985). Even though sociologists in this category typically admit that social factors are not the only causal factors in science,[1] they still argue that social factors are indispensable in scientific decision making.

On the other hand, according to the second view, the scientific community itself is conceived as a small society. In this small society, scientists have to negotiate to evaluate each other's work. Of course extra-scientific interests can come into such negotiations, but this is not a necessary factor when sociologists use the word 'social' in this sense. For example, Knorr-Cetina regards her research as 'social' because she consider "the objects of knowledge as the outcomes of processes which invariably involve more than one individual, and which normally involve individuals at variance with one another in relevant respects" (Knorr-Cetina 1981, 117). Sociologists in this category utilize various methodologies to analyze the consensus formation processes -- e.g., interview (Collins 1985),[2] participant observation (Latour and Woolgar [1979] 1986), conversational analysis (Garfinkel et al. 1981), and rhetorical analysis (Latour 1987; Gross 1990). Some of these sociologists go so far as to declare that everything is social (Latour and Woolgar 1986, 261).

Each of these views has proper problems. First, when sociologists argue for social causation, the problem is how to establish the alleged causal relationship. For example, through his review of the literature, Cole concludes that social constructivists fail to demonstrate any linkages between social processes and knowledge outcomes, namely the specific content of a scientific idea, like E= mc2 (Cole 1992, 61). Even the most representative study by Forman (1971) does not really establish a causal relationship, as many critics point out (e.g., Hendry 1980, Brush 1980, and Kraft and Kroes 1984). It is true that social constructivists find that scientists have many non-scientific commitments, but they never establish that if the commitments were different, the knowledge outcome would be affected by the change.

The problem with the claim that science is social because scientists negotiate is that this claim can make the word 'social' superfluous. For example, according to Tilly (1981), Latour and Woolgar's Laboratory Life (the most representative work in participant observation of science) corroborates Popper's view that successful scientists try to refute their own hypotheses. It is still true that sociologists can describe scientists' exchange in sociological terms, but if we can describe the same process in rationalistic terms, such sociological descriptions become superfluous.

1-2. Four objects of construction

Sismondo (1993) distinguishes four kinds of 'social construction' mainly by the object being constructed: (1) construction of institutions including knowledge and facts; (2) construction of scientific theories; (3) construction of artifacts in laboratories; (4) construction of the object of representation, namely, the reality (516). In the first two senses, 'construction' means that it is a result of an agreement. In the third sense, 'construction' is used almost literally. In the fourth sense, 'construction' is used as in Kantianism. According to Sismondo, Knorr-Cetina (1981) uses the word in the senses (1)~ (3), and Latour and Woolgar ([1979] 1986) use the word in all of these senses (Sismondo 1993, 527-536).

The problem with social constructivists is that they usually do not distinguish these four kinds of constructions. Even worse, they sometimes consciously conflate some of them. For example, in arguing for the claim that reality is socially constructed, Latour and Woolgar argue that (3) and (4) are basically the same thing ([1979] 1986, 174-183). Another common strategy is a conflation of (2) and (4), namely conflation of truth and what is regarded as true in a society. Even though I admit that sociologists have several interesting arguments relevant to realism-antirealism debate, I don't think that they have made the case that reality is socially constructed. I also thinks that artifacts are socially constructed in laboratories, but this fact has little philosophical significance when it does not support the social construction of reality. Of course I need more argument here, but I don't have enough space here, and this is somewhat beyond the scope of this paper.

1-3. what shall we incorporate into philosophy?

Then, what can we philosophers expect from the cooperation with the sociologists? My review of two senses of 'social' suggests that each of them has serious problems, but I think that the latter sense of 'social' study of science, namely study of scientific consensus formation can benefit philosophers. These studies give us a framework to pay equal attentions to scientific and extra-scientific factors, when extra-scientific factors are relevant. We can also learn from the studies of social causation. Even though they fail to establish causal relationships, their study of extra-scientific commitments of scientists can pose us a question: if these extra-scientific commitments are excluded from scientific consensus formation process, what is the mechanism which enables and maintains such an exclusion? As we will see later in this paper, Fuller and other philosophers develop their theory on these sociological insights.

Among four kinds of construction, as my above diagnosis suggests, I think that for now we can concentrate on (1) and (2), namely social construction of facts and theories. When social is taken in the second sense, I think sociologists have made interesting contributions on these matters, as will be reflected in the following arguments about socialized epistemology.

2. Socialized epistemology[3]

Now we know what kind of sociological findings to incorporate into philosophy. But the next question is, how? Even among the philosophers who recognize the importance of SSK literature, the epistemological theories they develop are fairly diverse. In this section, I consider the attempts to incorporate social aspects into the naturalized epistemology. My criticism of this kind of attempt applies to the naturalized epistemology in general, so let me start with the description of the naturalized epistemology itself.

2-1. Naturalized epistemology

So-called "naturalized epistemology" has its origin in Quine's paper "Epistemology naturalized" ([1969] 1994). In this paper, Quine observes that foundationalist attempts to establish theory of truth has failed, and his diagnosis of the reason of the failure is that they are dependent on the dogma of reductionism. To save epistemology from this situation, Quine proposes a new way to do epistemology. Now epistemology is not only conducted with scientific method, but epistemology is a science, or, more exactly, a part of psychology; "epistemology, or something like it, simply falls into place as a chapter of psychology and hence of natural science. It studies a natural phenomenon, viz., a physical human subject" (25). So, basically what we study in epistemology is relation between inputs to a human subject and outputs as descriptions of the external world by the subject. Since epistemology is supposed to provide basis for all kinds of science, including psychology, this makes epistemology a circular enterprise. But since foundationalist attempts have failed, maybe there is nothing wrong with circularity. Indeed, Neurath's boat metaphor implies this kind of circularity (26).[4]

A.I. Goldman, in his paper "What is justified belief?" attempts to redefine justification of beliefs in terms of such naturalistic view of epistemology. According to him, our belief is justified if it results from a reliable belief forming process, and a process is reliable if the process tend to produce true beliefs (Goldman's final definition is much more complicated; see Goldman 1992, 112-125). This view is often called 'reliablism'. This argument obviously presupposes that we know about the true state of the world and about our cognitive processes before we know what a justified belief is. This information is provided by psychology and other scientific fields. Again, this is circular, and presumably Goldman's reply to this charge is the same as Quine's.

Quine seems to regard the naturalized epistemology as a purely descriptive enterprise, while Goldman introduces a normative factor through obvious affirmative connotations of words like "justified" or "reliable." But at the same time Goldman tries to reject traditional a priori normativity. His discussion about "availability" is illuminating on this point (Goldman 1992, 173-174). Tversky and Kahneman (1973), Nisbett and Ross (1980) and many other psychologists have studied so-called "availability heuristics," namely the phenomena that people tend to assign higher frequency to things which come to mind easier than other things. For example, when asked to estimate the relative frequency that the letter 'r' appears at the beginning of a letter and the frequency that 'r' appears at the third place of a word, people consistently overestimate the former. Nisbett and Ross argues that this heuristic can lead to "serious judgmental errors" and therefore we need to distinguish legitimate and illegitimate use of this heuristic (1980, 23), but Goldman disagrees. If the heuristic is so stubborn that it is hard to us to catch the bias from it, maybe it is inappropriate to accuse the person of not noticing the bias. As Fuller points out, this is a peculiar application of the "ought implies can" principle (Fuller 1992a, 442). That is, since people cannot help using the availability heuristic, they do not have the obligation not to use it. Thus, even though Goldman admits the normative aspect of epistemology, he restricts the power of normative arguments by naturalistic considerations.

2-2. Epistemology socialized

many philosophers conceive socialized epistemology as an extension of naturalized epistemology (e.g. Goldman 1992, chapter 10; Kornblith 1994; Fuller 1988, chapter 11). For example, Goldman argues that social practices and institutions in science are justified when they tend to produce true beliefs (Goldman 1992, 192). Philosophers typically appeal to this kind of justification when they have to deal with extra-scientific commitments of individual scientists. Here are several examples. Hull (1988) argues that scientific changes can be explained in terms of evolutionary model. Scientists seek to enhance their conceptual inclusive fitness, and this activity leads to the selection of better ideas.[5] Goldman and Shaked (1991) shows that credit-seeking activity of scientists can lead to more true beliefs than truth-seeking activity, under some specific conditions. Kitcher (1993, chapter 8) contains a lot of interesting technical arguments on the relationship between individual motivation of scientists and communal rationality. First he deals with the problem of authority. He shows that epistemically sullied agents (who want to become the first discoverer of something) will rationally rely on other scientists' results under certain conditions. he also discuss division of cognitive labor and theory choice. To attain new discovery, cognitive diversity is desirable for community (under some situations), and sullied agents tend to attain more diversity than epistemically pure agents. Local autocracy can help diversity as well.[6]

The above philosophers are in naturalistic tradition not only in the sense that they are reliablists, but also in the sense they refrain from normative judgements. Even when they do make normative judgements, they obey the "ought implies can" principle in the above defined sense. For example Fuller cites Collins' sociological study about replication to illustrate this point (Fuller 1988, 268-269; obviously Fuller has changed his position later, as I discuss in the next section). Collins (1985) analyzes the gravity wave debate in the early 1970s, and concludes that exact replications of each other's experiments are almost impossible, and moreover the scientific community discourages such exact replications. If this is true, so Fuller argues, then, even if exact replications are philosophically desirable, scientists have no obligation for such replications.

2-3. What is wrong with naturalized (and socialized) epistemology?

I have two main objections to naturalized (and hence to socialized, too) epistemology. One is against reliablism, and the other is against the "ought implies can" principle.

My first objection is that even if traditional epistemological attempts have failed in some sense, this does not warrant the adoption of naturalized epistemology. As Devitt's elaboration of the argument for naturalized epistemology shows, the choice of naturalized epistemology can be conceived as the choice between two problematics, namely Cartesian skeptical problematic and naturalistic problematic (Devitt 1997, chapter 5). Cartesian skeptical problematic asks the question whether we have any reason to assume that we know something about the external world. Reductionists are motivated to provide a basis for such knowledge, and failed. Instantaneous solipsism may be justifiable in this problematic, but it is hardly a viable option. Devitt (and, I think, Quine, also) argues that this history of failure shows that the Cartesian problematic is unanswerable, and therefore uninteresting. Rather, we need to start from taking science for granted, and see what results from this starting point. This is naturalistic problematic.

I can agree that traditional attempts failed in some sense, for the sake of argument, but I certainly disagree that naturalistic problematic is the sole alternative. The failure of Cartesian skeptical problematic came from the requirement that knowledge should be absolutely certain (or at least highly probable). Even if this problematic has failed, we can modify it by changing the required degree of certainty. If we set the required degree of certainty reasonably high, we can rule out many implausible alternatives. Now, here is a revised skeptical problematic: choose the theory which has the highest degree of certainty (i.e. requires the lowest degree of reasonableness from skeptics) among viable alternatives. Please note that this problematic does not exclude circular justifications, because, for example, if all viable alternatives are circular, we should choose the most certain (circular) argument. Anyway, this problematic is not uninteresting at all. If I adopt this problematic, I cannot start simply assuming that we know about truth and our psychological processes. Reliablism itself should be examined by comparing it with other alternatives. Of course this argument does not refute reliablism, but at least it undermines a dogmatic acceptance of reliablism.

My second objection is directed to the "ought implies can" principle. First of all, naturalized epistemologists ignore subtle differences between normative judgements. Suppose that certain philosophically desirable process is psychologically or sociologically impossible. Maybe this is enough to say that scientists do not have the obligation to use the process, but still we can make a weaker normative judgement that the process is desirable (recommendable, advisable, etc.), and when someone manage to overcome the influence of the erroneous heuristics, we can praise it. Of course this kind of recommendation requires a point of view external to actual scientific decision processes, but this is exactly why we philosophers should be involved in this issue. Moreover, I think that naturalized epistemologists take psychological and sociological process too deterministic. In this respect, Fuller's recent argument against his own former view is illuminative (Fuller 1992). He still admits that psychological evidence on availability heuristic and other irrational methods is compelling, but now he thinks that introduction of social aspects can solve the problem: "if individuals are as resistant to rationality as the experimental evidence suggests, then it is probably more efficient to aim to compensate for cognitive deficiencies than to eliminate them outright. In other words, where the reasoner cannot be changed, change the reasoner's environment" (Fuller 1992, 444; italics in original). According to Fuller, this is another interpretation of "ought implies can," placing emphasis on "ought." In this interpretation, if we ought to do something, we should be able to find a way to fulfill the obligation, so we are better advised to keep looking for it. I think Fuller's argument is sound in general (though I think cognitive deficiencies themselves can be reduced by changing environment during childhood).

3. Fuller's social epistemology

As the argument at the end of the previous section shows, Fuller takes normative aspect of epistemology seriously, and develops his own alternative view on the desirable relationship between sociology and epistemology.

3-1. Philosophy of science as science policy-making

Steve Fuller proposes to resurrect normative epistemology as science policy-making, and to call this attempt "social epistemology" (Fuller 1988). Fundamental question of his social epistemology is: "how should the pursuit of knowledge be organized, given that under normal circumstances knowledge is pursued by many human beings, each working on a more or less well-defined body of knowledge and each equipped with roughly the same imperfect cognitive capacities, albeit with varying degrees of access to one another's activities?" ( Fuller 1988, 3). In short, this is a normative enterprise to look for better scientific institution, informed by psychology and sociology. The starting point of social epistemology is the doubt that "left to its own devices, science will not necessarily produce the sort of knowledge that we are interested in having" (Fuller 1992, 392). The reason we want knowledge is independent of science itself, and we can judge the efficacy of science from this outside point of view. For such judgements, Fuller proposes to use an experimental method. For example, we can conduct experiments taking independent variables such as "group size, communication constraints, and background information" and dependent variables such as "the sort of scientists, scientific audience, and knowledge commodity that is produced" (Fuller 1992, 405).[7] These experiments can decompose the overall effect into its working causal parts, and can also compensate for sociologists' interpretative biases (Fuller 1992, 404-405). Of course the experimental results are artificial in a sense, but this does not bother social epistemologists. If we find effective institutional structures in experimental settings, what social epistemologists may want to do is make "the world behave more like the laboratory than vice versa" (Fuller 1992, 406).

From this point of view, Fuller also redefines the boundary between context of justification and context of discovery, which is long discarded by social constructivists (Fuller 1996b). In a scientific field, there are often several opposing research traditions. Each of the traditions has its own procedures for discovery and justification, and as sociologists point out, these procedures are inseparably connected with each other. The role of scientific justification (as opposed to justifications inside a tradition) is to remove the idiosyncratic character of a scientific discovery reached by "a particular research tradition in a given culture" (Fuller 1996b, 168). This is the context of justification Fuller has in mind, and his normative social epistemology is supposed to work at this level.

One of the peculiarity of Fuller's argument is that he regards the point of view for the normative assessment cannot be purely epistemic -- it is always science policy making at the same time. He has several arguments why epistemic issue and policy-making issue are not separable. First, in his 1988 book, Fuller discusses the problem of distribution of knowledge, and claims that "crucial epistemological differences occur at the level of the different textual embodiments" (Fuller 1988, 273). I do not spend time on this argument because I do not understand what the crucial differences are. Fuller's another argument is that even if scientists want true information about their pursuit, this does not mean that they want it above all else (Fuller 1996a, 162). Any epistemic activity has associated costs, and any normative argument about science need to consider these costs. Sometimes he even argues that we are in a post-epistemic world in which mutual critical scrutiny of scientists can not work properly (Fuller 1994). The major problem is the size of scientific activity. Once, when scientific enterprise was smaller, "it was reasonable to presume that whatever one wrote would be subject to critical scrutiny by the relevant disciplinary community" (43). But now, since the number of scientists and their publications have remarkably increased, we cannot expect such ideal readers. The place a scientific research project is really scrutinized now is funding, the scrutiny is relative to the funder's interest (45). But if science is conducted to meet such interests, "to what extent, if any, is research any longer evaluated as products of inquiry?" (44). From these reasons, Fuller concludes that "the markets in which scientists currently conduct their business have expanded to the point of rendering obsolete the treatment of certain artifacts and skills as knowledge bearing" (45). In this sense, "science no longer exists" (ibid.). According to Fuller, philosophers overlook this situation because of "the subdivision between ethics and epistemology within professional philosophy," which "fosters the illusion that a clear distinction can be drawn between the moral and epistemologically relevant consequences of a given course of action" (ibid.). These are the reasons why Fuller thinks that normative epistemology is inevitably a science policy making.

3-2. Problems with Fuller's argument

I think that Fuller's argument has many virtues. As I said, I agree with his criticism of naturalized epistemology, and I think that he is right in that epistemology need a truly normative element. I also agree with him that, when we want to answer the question what scientists should do or what kind of institution should they have, we need to consider not only epistemic factors but also moral and political factors. However, I also think that Fuller has gone too far when he says that the distinction between epistemic and non-epistemic factors is an illusion. I think that the distinction is not only real but also useful.

To see the point, I would like to introduce the distinction between normative conclusions and normative considerations. As Fuller and sociologists he cites argue, in an actual scientific institution, epistemic elements and non-epistemic elements are inseparably intertwined. Hence our normative conclusions about such an institution, like "this institution is recommendable" or "it should be abandoned," should have both elements. So far, so good. But at the level of considerations to reach the conclusions, we may well consider epistemic and non-epistemic aspects separately. To reveal the level of normative consideration, it might be helpful to ask "why do you think that this institution is recommendable?" The person may mention several reasons including epistemic ones (like "because it tend to produce true beliefs") and non-epistemic ones (like "because it enhances social welfare"), but it is very unlikely that each of these reasons has both epistemic and non-epistemic elements. In this sense, epistemic reasons and non-epistemic reasons are discrete at the level of normative consideration. What we do to reach a normative conclusion is to weight these favorable and unfavorable reasons, and balance them to find whether the overall consideration is favorable or unfavorable. Now, it is easy to reconstruct epistemic part of such a consideration; all we have to do is to balance only epistemic reasons among the reasons.

What is the point of such a reconstruction? Even though we should count in all relevant considerations before we reach a dependable normative conclusion about a scientific institution, it is hard for a person to be an expert in all relevant areas. Here is the reason we need a division of cognitive labor in science studies; epistemologists mind exclusively epistemic parts, sociologists social parts, etc. If we arrange the institutional relation between epistemologists and sociologists properly, this specialization will result in a better choice than mixing up everything. Maybe Fuller replies that there is no epistemic aspect in science now, but this reply seems to be a legacy of the "ought implies can " principle in naturalized epistemology. If we really need epistemic aspects in science and current scientific institution does not have the aspect (actually I think he exaggerates the situation), what we need to do is to look for a way to resurrect epistemic aspects in scientific institution. Factual absence of epistemic aspects does not prohibit us to make epistemic normative judgements about science. Thus, I conclude that it is not only possible but also desirable that social epistemology concentrates on epistemic aspects of scientific institutions.

4. Social empiricism

4-1. Social rationality without individual rationality

Then, what does such an epistemology look like? Miriam Solomon's recent works on "social empiricism" suggests a way to proceed in that direction (Solomon 1992, 1994a, 1994b). Like naturalized epistemologists and Fuller, she also starts from psychological findings about human reasoning, like availability. Solomon's major concern is with a specific type of availability heuristic, namely the fact that scientists tend to overestimate the weight of evidence from their own field. Her favorite case study is the plate tectonics revolution in geology. As Stewart's (1990) and Carozzi's (1985) studies show, those who had had "Gondwana experience" (who have worked on the southern hemisphere materials relevant to Wegener's continental drift hypothesis) had strong tendency to accept continental drift, even though these materials were known to everyone in geological community. She also finds other hardly rational decision processes, like influence from peers and people in power (Solomon 1994a, 333-334; see also Glen 1982, 334-335 for the relevant material). Despite these biases of individual scientists, the final decision of the community, the acceptance of the plate tectonics theory, seems very rational.[8] Social empiricism tries to solve this paradoxical situation by introducing a clear distinction between individual level and society level. Namely, social empiricism maintains that "social groups can work to attain and even recognize epistemic goal without individual rationality or individual cognizance of the overall epistemic situation" (Solomon 1994b, 219). According to this view, these individual biases played a positive role for making a consensus for the empirically successful theory, by appropriately distributing cognitive effort.

This view may sound pretty much like the models developed by aforementioned naturalized epistemologists like Hull, Goldman and Shaked, and Kitcher. But there are several important differences. First, those naturalized epistemologists use rational self interests of scientists to explain diversity of research projects, but at the same time they assume scientific rationality at the individual level when scientists finally reach consensus. However, the evidence from the plate tectonics revolution does not support such an individual rationality (Solomon 1994a, 328-330). Social empiricism tries to explain a rational consensus of scientific community without reducing it to rationality of individual scientists. Rather, peer pressure and influence of powerful people is used to account for the consensus. Second, Solomon rejects reliablism, and claims that empirical success should be the measure of a good theory. That is, "a consensus is normatively appropriate if the theory selected has greater empirical success, and would not have been selected if it had not had such empirical success" (Solomon 1994a, 337). This is why she calls her position "empiricism." Finally, she emphasizes normative application. In the case of the plate tectonics revolution, biases worked very well. Then what we should learn is the appropriate distribution of biases to make sure such a success in the future (Solomon 1994b, 226-229). Her empiricism also provides an outside criterion to judge a consensus. So, for example, Solomon judges that the choice of the plate tectonics theory over its permanentist alternative during the sixties was appropriate, while the dismissal of another alternative, expantionism, was not appropriate at that time because both the plate tectonics theory and expantionism had enough empirical supports (Solomon 1994a, 337-338; See also LeGrand 1988, 224 for relevant material). This kind of purely normative judgement marks Solomon's position compared with naturalized epistemologists.

When compared with Fuller, Solomon's position can be seen as a revision of Fuller's. The major difference between them is that Solomon restrict her normative consideration to empirical success. She understand empirical success quite broadly, including technological success as well as predictive success, but still there is no science policy in her argument. As I argued in the previous section, this kind of specialization is possible and fruitful, given an appropriate institutional framework.

4-2. Problems with social empiricism

Even though I think that social empiricism is a promising approach to incorporate sociological findings about consensus formation into philosophical considerations, there are several problems to be solved before we apply this approach extensively.

The first problem is the possibility of collective rationality without individual rationality. She talks about the recognition of epistemic goal by social groups without individual cognizance (Solomon 1994b, 219). Does she assume a group mind or something? I think it is just a metaphorical expression, but obviously this is a point which requires further articulations. I think Margaret Gilbert's works on collective belief is helpful for such a task (Gilbert 1987, 1994). According to her it is obvious that we cannot reduce collective belief into individual beliefs. Her example is a food committee and a library committee with exactly the same member (Gilbert 1987, 189). It is quite plausible that the food committee believe different things from the library committee even in such a case. This difference comes from the fact that what an individual regards as appropriate for group consensus is independent of what the person believes personally. She elaborates a notion of joint acceptance depending on this distinction (Gilbert 1987, 194-195). Joint acceptance is maintained by its normative implication that when someone says something against jointly accepted opinion, others have right to rebuke the person (Gilbert 1994, 246-248). I think that her argument needs modification to be applied to scientific community, but basically she seems to provide a promising starting point.

The second problem with Solomon's argument is her empiricism. It seems to me that she assumes a very traditional empiricist model, a clear distinction between theory and observation. Then, how does she deal with theory-ladenness of observation? I don't have enough space to discuss this problem here, but my basic position is that theory and observation is a wrong way to divide scientific activity. Rather, as proposed by Suppes (1969) and developed by Mayo (1996) recently, science can be divided different levels of models, like primary models, experimental models and data models (Mayo 1996, chapter 5). In this picture, each level has theoretical and observational elements, but lower models become fairly independent from higher levels. This point needs further articulation, but this is not an appropriate place to do that.

Finally, Solomon should show that biasing factors she discusses are (or, at least, can be) distributed by some social mechanism, if she claims that we can learn about rationality from the history. For, if the rational consensus is a fortunate accidental result of a totally random distribution of biases, there is nothing we can learn from the case to improve existing institutions. This is a sociological question about the way a social organization works, and further cooperation between philosophers and sociologists will be required to find an answer.

5. Concluding remarks

In this paper, I have considered three different perspectives on the cooperation between sociologists and philosophers. Among them, I criticized socialized epistemology as an extension of naturalized epistemology because of its reliablism and its peculiar interpretation of the "ought implies can" principle. My criticism of Fuller's social epistemology is his failure to distinguish epistemic and non epistemic considerations in normative judgement about scientific institutions. Compared with these alternatives, Solomon's social empiricism seems to be a promising approach, even though there are a lot to be articulated about her position.

I would like to add one more comment. My strategy to criticize reliablism was not a direct denial, but a proposal of an alternative problematic, the revised skeptical problematic. My preference of Solomon's empiricism over reliablism is dependent on this problematic. Reliablism starts from taking entire science for granted. Solomon's empiricism, on the other hand, starts from a subset of science, our knowledge about empirical success. In general, the less the number of the assumptions is, the more the plausibility of the conclusion is. Thus my skeptical problematic prefers Solomon to reliablism.


[1] See, for example, Bloor 1991, 165-166, Forman 1971, 3, Collins 1994, 501-503. Pinch and Bijker are notable exceptions, but they are arguing for sociology of technology, not for sociology of science in general (Pinch and Bijker 1987, 18-19).

[2] Collins seems to use the word 'social' in both meanings, without clearly distinguishing. See Collins 1994, 503.

[3] Usually terms 'socialized epistemology' and 'social epistemology' are used interchangeably, but in this paper I use the former to denote extension of naturalized epistemology, and the latter to denote Fuller's position.

[4] Devitt 1997 elaborates the same line of argument in great detail. My manuscript B analyzes Devitt's argument critically.

[5] For more details and my evaluation of Hull's argument, see my 1996.

[6] My manuscript C discusses problems with Kitcher's project.

[7] For actual examples of such an experiment, see Gorman et al. (1984) and Rosenwein and Gorman (1995). For a theoretical account of science simulation, see Gorman and Rosenwein (1995). I am skeptical about the relevance of these works to actual science, but I do not have space to argue about this topic here.

[8] Actually this interpretation of the plate tectonics revolution is controversial. There are many others who emphasize the rationality of individual scientists in their theory choice. My manuscript D reviews these other interpretations, and also contains more about Solomon's own interpretation of this case.

References (my unpublished manuscripts are available at the following web site:

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