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Hull Symposium -- PSA 1990
by Noretta Koertge

Introduction:

David Hull's book provides an evolutionary account of the development of science which pays attention to both the social and conceptual aspects of that process.
Unlike most philosophers, who only invoke Darwinian metaphors in a casual way, Hull takes the analogy between the biological evolution of species and the growth of scientific knowledge quite seriously and by providing abstract definitions of terms such as replicator, interactor and lineage, he makes it possible for us to see clearly the structural similarities between the two historical processes.
Others here today will comment on how tight that analogy really is. I must remark in passing that I have never understood the intense interest evolutionary which epistemologists take in this comparison. Surely our major job is to understand how science works, perhaps by using evolutionary theory as a fallible heuristic, but nothing seems to hinge on the extent of the formal analogy. My main concern would be with the extent to which the evolutionary analogy illuminates what is distinctive about scientific development as opposed to other branches of intellectual history. For example, Elaine Pagel's story of the struggle between the early Gnostics and what we would now consider the more orthodox variants of Christianity could be translated into quasi-Darwinian terms as follows:
In the first few centuries after the death of Jesus, two important theological systems (cf. genotypes) existed. Each had its own gospels. The four orthodox gospels (Matthew, Mark, Luke, John) spoke of the bodily resurrection of Christ. The gnostic gospels (e.g. those of Mary Magdalene and Philip), on the other hand, spoke only of spiritual resurrection and implied that the post-crucifixation sightings of Jesus were really mystical visions, not observation reports. These two theologies were embodied in and influenced the actions of two groups of Christians (cf. phenotypes). The orthodox group were more successful in gaining converts, not because of any intrinsic theological superiority, but because their doctrine of apostolic succession (passed down from Peter through ordination) gave their movement more stability. The leadership roles amongst the gnostics were more fluid because they depended on the charismatic and visionary powers of individuals, qualities which were much more difficult to operationalize. As a result, Gnostic Christianity literally went extinct - there were no extant replications of many of the Gnostic gospels until the discoverry in 1945 of a bunch of manuscripts in a jar in Egypt.
The point of my example is this: The part of Hull's account which parallels evolutionary biology does not solve the demarcation problem - it does not describe the distinctive aspects of the growth of scientific knowledge. What must be added to the general evolutionary account are the scientific norms which Hull summarizes by the slogan of curiosity, checking, and credit.
Theologians do not, in general, place high value on any of the three C's. But scientists are carefully trained to do so and it is these norms which determine how the struggle between competing scientific theories is to be conducted and which differentiate the discussions of the Nobel Prize Committee from religious discussions about who should or should not be canonized. (I am not denying that politics plays a role in each; but I do claim that the standards of appraisal differ.)
So I want to now turn away from the Spencerian swamp of evolutionary epistemology and concentrate instead on what Hull says about the distinctive values and social practices of science, especially what he says about the roles of competition, cooperation and credit in organized science and how they contribute to the growth of scientific knowledge.
Most of my remarks will be a re-presentation and/or sympathetic extension of David's account, but at the end I think my approach may deviate from what he had in mind, but maybe not - we'll see!

The Problem of Whether the Concern About Credit Helps or Hinders Science
Before I read Hull, I think if someone has asked me about the significance of the emphasis which scientists place on the ways in which credit is apportioned in science, I might have said something like the following:
The "real" value/purpose of footnotes is to direct the interested reader to a place where they can get additional information on the subject. Who did the experiment or formulated the theory is "really" not very important, although it does provide a way of assigning responsibility for bad work. It is also sometimes important to know how many different laboratories have replicated a particular experiment.
As far as credit is concerned, counting citations, etc. is something which only sociologists, tenure/promotion committees, funding panels, and other folks who haven't time to read the literature have any need to do. "Real" scientists are motivated by curiosity and the joy of problem solving; the essential ingredients of a scientific community are the traditional Mertonian norms of universalism, disinterestedness, and communalism. All of this striving for personal recognition is at best peripheral to the process of science.
As for priority disputes, I would have said that these are the legitimate concerns only for patent lawyers and hero-worshipping historians (still under the spell of romantic theories of genius). A "real" scientist is passionately concerned that the solutions to important problems be found and checked by others, but it can't possibly "really" matter to science whose discovery was first. Maybe sociobiologists can explain why (male) scientists have so much "paternity anxiety" or worry so much about who was the first to score the big "breakthrough". All of this is embarrassing nonsense which may tell us something about the pettiness and immaturity of scientists (which is exacerbated by today's funding squeeze) but has nothing to do with science "comme il faut".
However, after reading Hull I am prepared to seriously entertain the idea that the credit practices of scientists cannot be ignored by any adequate theory of science and that credit does play an important role in the furthering of intellectual progress in science. I may be less optimistic than David, however, about how efficiently our present credit system functions. And I also think we need to have a good analysis of exactly how the present reward system benefits science. It is not good enough just to say, science is doing pretty well so our present credit system must be O.K.

Why Curiosity and Checking Are Not Enough

To motivate Hull's emphasis on the reward system of science and to begin our analysis of how it works, let us do a typical social philosophy thought-experiment in which we start out with isolated individuals and then assemble them into an efficient, scientific community. What new motivational ingredients would we need to inculcate? What special social norms would need to emerge? And since we are focusing on credit, let us also assume that our individual scientists are already well-equipped with curiosity and are already personally intriqued by the various types of problems which trigger scientific inquiry - problems arising from violated expectations, unexplained regularities, ununified bodies of knowledge, etc.
Let us also assume that they already have a propensity to subject proposed solutions to problems to critical scrutiny and have already realized that it is a good idea to have independent, skeptical collaborators to scrutinize observation claims, come up with cogent objections to other people's theories, etc. So, the present thought experiment presupposes that the institutions which facilitate scientific curiosity and empirical checking are already in place. We now ask, why isn't this enough? Why do we need to add a concern for individual credit in order to make our New Atlantis work?
The general answer is, I think, fairly simple. We want scientists to solve new problems, ones which no one yet knows the answer to, and we want them to publish their solutions. Lest we take all of this for granted, we should remember that children routinely satisfy their curiosity and hone their problem-solving skills by re-discovering Archimedes' Principle or playing with Rubick's cubes. One tension in science education is how to teach students the skills necessary for and the satisfactions of solving problems for themselves (in which case the novelty of their solutions is unimportant) while also encouraging them to look up answers to questions in authoritative reference works and to devote their energies to working on new projects. And there are educated adults, many of them excellent college teachers, whose active curiosity makes them life-long readers of "Great Books" but who have few aspirations to make novel contributions.
Satisfying one's personal curiosity does not insure communal progress. For the latter to occur, we need to make easily available combined communal information (e.g., libraries), we need to insure that people work on genuinely new problems (e.g., by requiring literature searches), and we need to reward people for actually publishing any solutions which they obtain, instead of secretly gloating that they know something which no one else does (hence, the publish-or-perish ethos).
Hull points out that in the past, scientists were often reluctant to make their results public. There was (and is) of course a tradition of passing on craft skills and secrets only to apprentices (e.g., alchemy, Stradavarius' violins) and until the patent-system was developed it would be silly to divulge technological innovations.
But gentlemen scientists also buried results in desk drawers out of laziness, or caution, or failure of nerve - or because the incentives and opportunities to publish were deficient. For example, here is Dijksterhuis' commentary on his countryman, Isaac Beeckman:
"Beeckman showed the same defects in the matter of science as Leonardo da Vinci. Both were deficient in the tenacity of purpose and powers of concentration required to systematize, finish, record, and publish their inquiries, even if only in one field. Of Faraday's motto: `Work, Finish, Publish', they only took to heart the first injunction. In consequence they either did not advance science at all, or at least to a much smaller extent than they might have done.
"Those of Beeckman's ideas which are going to be described here do not therefore really form a link in the chain of development under consideration. However, they are of value because they give the reader some notion of the scientific thought of a gifted man of the early seventeenth century." (The Mechanization of the World Picture, p. 330)
"We shall see more of Beeckman's independent and frequently original way of thinking later: it is to be regretted that this candle never stood on a candle-stick." (ibid., p. 333)
Although today we tend to think that it is "natural" to want to solve problems no one else has ever solved before and to get public credit for it, I think even a brief look at the early history of science and especially at traditional societies (cf. Kemal's Mehmet, My Hawk) reminds us that such a drive is not to be taken for granted and must in fact be carefully shaped through scientific institutions. (Every human being may be curious and want some kind of recognition from their peers, but the kinds of things scientists get curious about and the kinds of credit that they find rewarding are both unusual tastes which are probably acquired.)
Let us now look in a little more detail at how the credit system in science works so that we can eventually ask how efficient it is in fostering scientific progress. Hull's description of the publishing/citation system quickly reveals just how complex the credit system is. Perhaps we can begin to analyze and evaluate it by looking at how credit considerations enter in at each step of the scientific process as philosophers would describe it. (Here I follow a quasi-Popperian schema.) Again I will adopt a thought-experiment strategy. Let us assume that scientists have the mundane proximate aim of maximizing personal recognition. How well will the behavior appropriate to such an aim coincide with the traditional ultimate aim of understanding the universe?
In the sketch which follows I will emphasize the congruence between these goals (because that is what I found surprising).
(i) Choice of problem: If our immediate aim is to get published in scientific journals, we should choose problems which haven't been solved yet, but which are ripe for solution. (It is generally difficult to publish unsuccessful solution attempts or interim reports.) It may be wise to form a team so as to be able to tackle problems which others aren't equipped to solve and in order to solve problems more quickly. Of course, this means we'll have to share credit with our co-authors. We also will need to be able to assess the competence of prospective teammates.
We should also choose a problem whose solution will be of interest to our peers (otherwise they won't cite our work). This tends to lead a clustering of research efforts around hot topics which means there is more data/theoretical speculations around that topic for everyone to use. But it also promotes a healthy division of labor because it encourages research teams to choose not just problems which they have a good chance of eventually solving, but ones which they also have a good chance of solving first.
(ii) Working out a tentative solution: Since the first publication often gets the most positive citations, we must work rapidly and secretly, especially if other individuals or teams are pursuing similar lines of inquiry. This is a time for team camaraderie, brainstorming, and constructive criticism of conjectures. We will look for promising helpful hints while refereeing our competitor's grant-proposals or even their submitted journal articles (although note that in scientific journals submission dates are published). On the other hand, we will be reticent to share preliminary results with anyone who might scoop us. This will also protect our own reputations if the conjecture we're working on turns out to be way off-base.
Once we have a solution which has passed preliminary appraisals, we must decide when to publish it. This is a complicated choice. The reasons for publishing as soon as possible are obvious: if we are right, we want to get credit for being first. However, as Hull emphasizes, there are also lots of reasons not to rush into print. If we are quickly shown to be wrong, our reputations are likely to suffer somewhat. (This non-Popperian attitude towards refuted bold conjectures has the function of pruning the literature a little bit. Note that the greater the reward for being first, the greater should be the penalty for being wrong if the literature is not to deteriorate.) There is yet another consideration: if our conjecture is correct, it will generally lead to other lines of productive research. By temporarily delaying publication, we can explore these ramifications at our leisure and publish everything at once!
(iii) Appraisal of the tentative solution: Ignoring for the moment the pre-publication networks in science, the first hurdle that our tentative solution has to pass is the journal review process.
In order to function well, the institutions which regulate publishing in science have to balance a variety of desiderata. Science (and the public) benefits when results are published, so there must be opportunities and incentives to publish. On the other hand, it is imperative to maintain quality control over what is published, so one needs to prevail on experts in each field to take time off from their own research to referee articles. Why should they consent to undertake these time-consuming and often unpleasant activites? Well, as any journal editor knows, not everyone does consent. It is in every scientist's cognitive interest to keep the communal knowledge store as reliable as possible but are there any mundane (credit-related) reasons for doing so? Well, as I pointed out above, it's always nice to have advance knowledge of what other people working in your area are up to. Furthermore, an excellent way to make sure your own ideas are taken seriously (thus gaining you credit while increasing their fitness) is to eliminate, or at least point out the weaknesses in, rival viewpoints.
The form of appraisal most emphasized by philosophers is that of varied and severe empirical testing, but a scientist looking for professional credit will not spend time performing experiments which are unlikely to result in a significant number of citations. So routine replications are out, tests of theories which are of low interest are out, even refutations of other people's popular theories will be of rather low priority (because they will probably not cite your results except to explain them away) unless the refutated theory is in direct competition with your groups own pet conjecture in which case your allies will cite it extensively. (One is reminded here of Lakatos' cognitive claim that there are no refutations, only superceded research programmes.) Under the credit system, bad theories don't die - no refutation of them may ever appear in print; they merely fade from view as their competitors get more citations.


The Problem of Maintaining the Credit System - Why Idealism is Important After All

Hull emphatically debunks the romantic myth of scientist as the objective, altruistic problem-solver whose only interest is that Nature be understood (and no matter who wins the Nobel Prize for being the first to probe her inner-most secrets). Scientists, like everyone else, want credit for their successes. However, Hull just as adamantly opposes the cynical view that since scientists que scientists are motivated by mundane ambitions, the products of their inquiry have no special cognitive status. This would be like arguing that since business men and professional athletes are both "in it for the money", it makes no difference whether you put Donald Trump or Magic Johnson on the basketball court! The crucial question is not whether scientists want credit; what matters is which activities they get credit for. Do the proximate rewards reinforce the ultimate aims of science? Can scientists "do well by doing good" science?
In the above analysis, I followed Hull in emphasizing the nice fit between what we might call the proximate mundane goals of professional success and the ultimate noble aims of the search for scientific understanding. Yet philosophy of biology reminds us how easy it is to make up "just-so" stories which render any trait you like adaptive. And philosophers of social science have taught us to be skeptical of easy functionalist analyses which emphasize the beneficial effects of the potlach, cargo cults, sacred cows, primitive warfare and witch burning.
Could we not also tell a pessimistic story about how the lust for quick publications and citations discourages scientists from tackling difficult problems which would take a long time to solve but which are nevertheless important? About how too much emphasis on credit can lead to the exploitation of graduate students, the mistreatment of laboratory animals, irresponsible methodological shortcuts, the practice of publishing virtually the same article in several places, unfair hiring practices, even outright fraud?
Even Hull's own optimistic analyses indicate that the balance between the cooperative and competitive aspects of science is a rather fine one. We note that some professions are not so lucky as science has been so far. The qualities and behaviors required to be a successful politician in an age of TV elections are almost contrary to those which contribute to statesmanship. And there are fewer professional incentives for doctors to stay abreast of new medical developments (unless their patients read about them in the popular press and demand them) than there are for scientists to keep up in their fields. When there is a dissonance between the success structure and internal aims, such as in medicine and politics, we need to focus on institutional reforms, where the direction of the reform is dictated by the internal aims of medicine (which are why society values it in the first place).
Or consider the case of professional sports, which is like science in having a good congruence between mundane success (reflected in salaries) and internally defined excellence (extraordinary sporting performances). It would at first appear that even if athletes were just in it for the money, they would have to play just as well. So one might argue that mundane motivations are sufficient for do not harm sports as long as there is a strong correlation between salary and batting averages.
Yet perhaps it is not just romanticism which makes us suspicious of this cozy conflation of the sacred and the secular. What if coaches become reluctant to call for a sacrifice bunt (because players want to keep their averages up)? What if salaries come to depend on a player's charismatic box-office appeal, not just on box scores? Won't people playing primarily for money be easier prey for point-shaving deals with gamblers?
The general point is this: Any congruence between careerism and love of the professional activity is precarious enough that we are ill-advised to abandon our romantic-sounding rehearsals of the internal aims of science or sport.
When a profession's reward system is consonant with the goals of that profession it is indeed possible to do good by doing well. But we should never forget the primary importance of doing good.
I will close with an anecdote. I once asked a seminar of graduate students how difficult it would be to completely fabricate their Ph.D. dissertation and get away with it. After they got over their initial shock, many of them answered that it would be quite easy. Well, why don't you do it, I asked. There was an embarrassed silence and finally the political scientist, whose survey research project we all agree would be the easiest to fake, answered" "Because it wouldn't be any fun? I want to know what my experimental subjects really think?"
Scientists want credit, yes. But what they want credit for is discovering interesting truths. It's the last part that most sociologists miss entirely. David doesn't miss it -- but perhaps we disagree on how important it is to keep harping on it. But of course his book was published before Colorado used five downs to win a game!


values and social practices of science, especially what he says about the roles of competition, cooperation and credit in organized science and how they contribute to the growth of scientific knowledge.
Most of my remarks will be a re-presentation and/or sympathetic extension of David's account, but at the end I think my approach may deviate from what he had in mind, but maybe not - we'll see!

The Problem of Whether the Concern About Credit Helps or Hinders Science
Before I read Hull, I think if someone has asked me about the significance of the emphasis which scientists place on the ways in which credit is apportioned in science, I might have said something like the following:
The "real" value/purpose of footnotes is to direct the interested reader to a place where they can get additional information on the subject. Who did the experiment or formulated the theory is "really" not very important, although it does provide a way of assigning responsibility for bad work. It is also sometimes important to know how many different laboratories have replicated a particular experiment.
As far as credit is concerned, counting citations, etc. is something which only sociologists, tenure/promotion committees, funding panels, and other folks who haven't time to read the literature have any need to do. "Real" scientists are motivated by curiosity and the joy of problem solving; the essential ingredients of a scientific community are the traditional Mertonian norms of universalism, disinterestedness, and communalism. All of this striving for personal recognition is at best peripheral to the process of science.
As for priority disputes, I would have said that these are the legitimate concerns only for patent lawyers and hero-worshipping historians (still under the spell of romantic theories of genius). A "real" scientist is passionately concerned that the solutions to important problems be found and checked by others, but it can't possibly "really" matter to science whose discovery was first. Maybe sociobiologists can explain why (male) scientists have so much "paternity anxiety" or worry so much about who was the first to score the big "breakthrough". All of this is embarrassing nonsense which may tell us something about the pettiness and immaturity of scientists (which is exacerbated by today's funding squeeze) but has nothing to do with science "comme il faut".
However, after reading Hull I am prepared to seriously entertain the idea that the credit practices of scientists cannot be ignored by any adequate theory of science and that credit does play an important role in the furthering of intellectual progress in science. I may be less optimistic than David, however, about how efficiently our present credit system functions. And I also think we need to have a good analysis of exactly how the present reward system benefits science. It is not good enough just to say, science is doing pretty well so our present credit system must be O.K.

Why Curiosity and Checking Are Not Enough

To motivate Hull's emphasis on the reward system of science and to begin our analysis of how it works, let us do a typical social philosophy thought-experiment in which we start out with isolated individuals and then assemble them into an efficient, scientific community. What new motivational ingredients would we need to inculcate? What special social norms would need to emerge? And since we are focusing on credit, let us also assume that our individual scientists are already well-equipped with curiosity and are already personally intriqued by the various types of problems which trigger scientific inquiry - problems arising from violated expectations, unexplained regularities, ununified bodies of knowledge, etc.
Let us also assume that they already have a propensity to subject proposed solutions to problems to critical scrutiny and have already realized that it is a good idea to have independent, skeptical collaborators to scrutinize observation claims, come up with cogent objections to other people's theories, etc. So, the present thought experiment presupposes that the institutions which facilitate scientific curiosity and empirical checking are already in place. We now ask, why isn't this enough? Why do we need to add a concern for individual credit in order to make our New Atlantis work?
The general answer is, I think, fairly simple. We want scientists to solve new problems, ones which no one yet knows the answer to, and we want them to publish their solutions. Lest we take all of this for granted, we should remember that children routinely satisfy their curiosity and hone their problem-solving skills by re-discovering Archimedes' Principle or playing with Rubick's cubes. One tension in science education is how to teach students the skills necessary for and the satisfactions of solving problems for themselves (in which case the novelty of their solutions is unimportant) while also encouraging them to look up answers to questions in authoritative reference works and to devote their energies to working on new projects. And there are educated adults, many of them excellent college teachers, whose active curiosity makes them life-long readers of "Great Books" but who have few aspirations to make novel contributions.
Satisfying one's personal curiosity does not insure communal progress. For the latter to occur, we need to make easily available combined communal information (e.g., libraries), we need to insure that people work on genuinely new problems (e.g., by requiring literature searches), and we need to reward people for actually publishing any solutions which they obtain, instead of secretly gloating that they know something which no one else does (hence, the publish-or-perish ethos).
Hull points out that in the past, scientists were often reluctant to make their results public. There was (and is) of course a tradition of passing on craft skills and secrets only to apprentices (e.g., alchemy, Stradavarius' violins) and until the patent-system was developed it would be silly to divulge technological innovations.
But gentlemen scientists also buried results in desk drawers out of laziness, or caution, or failure of nerve - or because the incentives and opportunities to publish were deficient. For example, here is Dijksterhuis' commentary on his countryman, Isaac Beeckman:
"Beeckman showed the same defects in the matter of science as Leonardo da Vinci. Both were deficient in the tenacity of purpose and powers of concentration required to systematize, finish, record, and publish their inquiries, even if only in one field. Of Faraday's motto: `Work, Finish, Publish', they only took to heart the first injunction. In consequence they either did not advance science at all, or at least to a much smaller extent than they might have done.
"Those of Beeckman's ideas which are going to be described here do not therefore really form a link in the chain of development under consideration. However, they are of value because they give the reader some notion of the scientific thought of a gifted man of the early seventeenth century." (The Mechanization of the World Picture, p. 330)
"We shall see more of Beeckman's independent and frequently original way of thinking later: it is to be regretted that this candle never stood on a candle-stick." (ibid., p. 333)
Although today we tend to think that it is "natural" to want to solve problems no one else has ever solved before and to get public credit for it, I think even a brief look at the early history of science and especially at traditional societies (cf. Kemal's Mehmet, My Hawk) reminds us that such a drive is not to be taken for granted and must in fact be carefully shaped through scientific institutions. (Every human being may be curious and want some kind of recognition from their peers, but the kinds of things scientists get curious about and the kinds of credit that they find rewarding are both unusual tastes which are probably acquired.)
Let us now look in a little more detail at how the credit system in science works so that we can eventually ask how efficient it is in fostering scientific progress. Hull's description of the publishing/citation system quickly reveals just how complex the credit system is. Perhaps we can begin to analyze and evaluate it by looking at how credit considerations enter in at each step of the scientific process as philosophers would describe it. (Here I follow a quasi-Popperian schema.) Again I will adopt a thought-experiment strategy. Let us assume that scientists have the mundane proximate aim of maximizing personal recognition. How well will the behavior appropriate to such an aim coincide with the traditional ultimate aim of understanding the universe?
In the sketch which follows I will emphasize the congruence between these goals (because that is what I found surprising).
(i) Choice of problem: If our immediate aim is to get published in scientific journals, we should choose problems which haven't been solved yet, but which are ripe for solution. (It is generally difficult to publish unsuccessful solution attempts or interim reports.) It may be wise to form a team so as to be able to tackle problems which others aren't equipped to solve and in order to solve problems more quickly. Of course, this means we'll have to share credit with our co-authors. We also will need to be able to assess the competence of prospective teammates.
We should also choose a problem whose solution will be of interest to our peers (otherwise they won't cite our work). This tends to lead a clustering of research efforts around hot topics which means there is more data/theoretical speculations around that topic for everyone to use. But it also promotes a healthy division of labor because it encourages research teams to choose not just problems which they have a good chance of eventually solving, but ones which they also have a good chance of solving first.
(ii) Working out a tentative solution: Since the first publication often gets the most positive citations, we must work rapidly and secretly, especially if other individuals or teams are pursuing similar lines of inquiry. This is a time for team camaraderie, brainstorming, and constructive criticism of conjectures. We will look for promising helpful hints while refereeing our competitor's grant-proposals or even their submitted journal articles (although note that in scientific journals submission dates are published). On the other hand, we will be reticent to share preliminary results with anyone who might scoop us. This will also protect our own reputations if the conjecture we're working on turns out to be way off-base.
Once we have a solution which has passed preliminary appraisals, we must decide when to publish it. This is a complicated choice. The reasons for publishing as soon as possible are obvious: if we are right, we want to get credit for being first. However, as Hull emphasizes, there are also lots of reasons not to rush into print. If we are quickly shown to be wrong, our reputations are likely to suffer somewhat. (This non-Popperian attitude towards refuted bold conjectures has the function of pruning the literature a little bit. Note that the greater the reward for being first, the greater should be the penalty for being wrong if the literature is not to deteriorate.) There is yet another consideration: if our conjecture is correct, it will generally lead to other lines of productive research. By temporarily delaying publication, we can explore these ramifications at our leisure and publish everything at once!
(iii) Appraisal of the tentative solution: Ignoring for the moment the pre-publication networks in science, the first hurdle that our tentative solution has to pass is the journal review process.
In order to function well, the institutions which regulate publishing in science have to balance a variety of desiderata. Science (and the public) benefits when results are published, so there must be opportunities and incentives to publish. On the other hand, it is imperative to maintain quality control over what is published, so one needs to prevail on experts in each field to take time off from their own research to referee articles. Why should they consent to undertake these time-consuming and often unpleasant activites? Well, as any journal editor knows, not everyone does consent. It is in every scientist's cognitive interest to keep the communal knowledge store as reliable as possible but are there any mundane (credit-related) reasons for doing so? Well, as I pointed out above, it's always nice to have advance knowledge of what other people working in your area are up to. Furthermore, an excellent way to make sure your own ideas are taken seriously (thus gaining you credit while increasing their fitness) is to eliminate, or at least point out the weaknesses in, rival viewpoints.
The form of appraisal most emphasized by philosophers is that of varied and severe empirical testing, but a scientist looking for professional credit will not spend time performing experiments which are unlikely to result in a significant number of citations. So routine replications are out, tests of theories which are of low interest are out, even refutations of other people's popular theories will be of rather low priority (because they will probably not cite your results except to explain them away) unless the refutated theory is in direct competition with your groups own pet conjecture in which case your allies will cite it extensively. (One is reminded here of Lakatos' cognitive claim that there are no refutations, only superceded research programmes.) Under the credit system, bad theories don't die - no refutation of them may ever appear in print; they merely fade from view as their competitors get more citations.


The Problem of Maintaining the Credit System - Why Idealism is Important After All

Hull emphatically debunks the romantic myth of scientist as the objective, altruistic problem-solver whose only interest is that Nature be understood (and no matter who wins the Nobel Prize for being the first to probe her inner-most secrets). Scientists, like everyone else, want credit for their successes. However, Hull just as adamantly opposes the cynical view that since scientists que scientists are motivated by mundane ambitions, the products of their inquiry have no special cognitive status. This would be like arguing that since business men and professional athletes are both "in it for the money", it makes no difference whether you put Donald Trump or Magic Johnson on the basketball court! The crucial question is not whether scientists want credit; what matters is which activities they get credit for. Do the proximate rewards reinforce the ultimate aims of science? Can scientists "do well by doing good" science?
In the above analysis, I followed Hull in emphasizing the nice fit between what we might call the proximate mundane goals of professional success and the ultimate noble aims of the search for scientific understanding. Yet philosophy of biology reminds us how easy it is to make up "just-so" stories which render any trait you like adaptive. And philosophers of social science have taught us to be skeptical of easy functionalist analyses which emphasize the beneficial effects of the potlach, cargo cults, sacred cows, primitive warfare and witch burning.
Could we not also tell a pessimistic story about how the lust for quick publications and citations discourages scientists from tackling difficult problems which would take a long time to solve but which are nevertheless important? About how too much emphasis on credit can lead to the exploitation of graduate students, the mistreatment of laboratory animals, irresponsible methodological shortcuts, the practice of publishing virtually the same article in several places, unfair hiring practices, even outright fraud?
Even Hull's own optimistic analyses indicate that the balance between the cooperative and competitive aspects of science is a rather fine one. We note that some professions are not so lucky as science has been so far. The qualities and behaviors required to be a successful politician in an age of TV elections are almost contrary to those which contribute to statesmanship. And there are fewer professional incentives for doctors to stay abreast of new medical developments (unless their patients read about them in the popular press and demand them) than there are for scientists to keep up in their fields. When there is a dissonance between the success structure and internal aims, such as in medicine and politics, we need to focus on institutional reforms, where the direction of the reform is dictated by the internal aims of medicine (which are why society values it in the first place).
Or consider the case of professional sports, which is like science in having a good congruence between mundane success (reflected in salaries) and internally defined excellence (extraordinary sporting performances). It would at first appear that even if athletes were just in it for the money, they would have to play just as well. So one might argue that mundane motivations are sufficient for do not harm sports as long as there is a strong correlation between salary and batting averages.
Yet perhaps it is not just romanticism which makes us suspicious of this cozy conflation of the sacred and the secular. What if coaches become reluctant to call for a sacrifice bunt (because players want to keep their averages up)? What if salaries come to depend on a player's charismatic box-office appeal, not just on box scores? Won't people playing primarily for money be easier prey for point-shaving deals with gamblers?
The general point is this: Any congruence between careerism and love of the professional activity is precarious enough that we are ill-advised to abandon our romantic-sounding rehearsals of the internal aims of science or sport.
When a profession's reward system is consonant with the goals of that profession it is indeed possible to do good by doing well. But we should never forget the primary importance of doing good.
I will close with an anecdote. I once asked a seminar of graduate students how difficult it would be to completely fabricate their Ph.D. dissertation and get away with it. After they got over their initial shock, many of them answered that it would be quite easy. Well, why don't you do it, I asked. There was an embarrassed silence and finally the political scientist, whose survey research project we all agree would be the easiest to fake, answered" "Because it wouldn't be any fun? I want to know what my experimental subjects really think?"
Scientists want credit, yes. But what they want credit for is discovering interesting truths. It's the last part that most sociologists miss entirely. David doesn't miss it -- but perhaps we disagree on how important it is to keep harping on it. But of course his book was published before Colorado used five downs to win a game!