Unconceived Alternatives

Kyle Stanford from UC-Irvine was here for a visit this past weekend, and talked about his novel argument against scientific realism. I thought there was a problem with the argument, but I now think maybe not.

Realism, here, is the epistemic thesis that we have good reason to think that the our present theories in the more mature sciences are true (or, at least, that the terms for unobservables in such theories succeed in referring). Kyle’s concern about this thesis derives from the fact that scientists are not that good at conceiving of all the alternatives to the theories that they propose.

On one level, this point is obvious: Newton didn’t, and in some interesting way, couldn’t conceive of quantum mechanics. The realist has a rejoinder that Kyle was willing to grant: exceptionalism. The exceptionalism response says that we now have a mature science and that the explanatory successes are sufficient to undermine the inductive argument from past failures to conceive of alternatives. In short, our situation is different from the situation of past great scientists, and so the induction fails.

Kyle’s response is to consider what he calls “close call” situations–cases where the alternative theories are readily available and well-confirmed by the evidence. So what he’s looking for are historical cases where a famous theorist seems incapable of formulating an alternative to their present approach to a problem.

One example Kyle used involves theories of inheritance, and relationship between Darwin’s theory of pangenesis and Galton’s alternative stirp theory. What’s interesting is that Darwin’s theory is a causal chain theory, and Galton’s a common cause theory, but Darwin simply couldn’t grasp Galton’s theory, even when he read Galton’s paper and corresponded with him about it. He keeps saying he doesn’t get it, doesn’t understand, and he never got the idea of a common cause alternative to his own theory. (This reminds me of some of my old professors–ossification of the mind perhaps, and an inability to comprehend new approaches. The sad part is that when you get to this point, you can’t detect it because once you get there you’ll think that it’s the result of the younger crowd just not being as good…and each side’s ad hominem cancels out the other…)

The correspondence is fairly compelling here–Darwin just didn’t get it. So Kyle has one example of the sort he wants–a “close call” situation where alternatives remain unconceived.

What I wanted to know about is how to test the unconceived alternative hypothesis. I understand what a confirming instance will look like–that’s pretty clear in the Darwin/Galton case. What I want to know is what a disconfirming instance will look like.

When we don’t find the textual evidence for unconceived alternatives, what conclusion will we draw? I expect we’ll just move on to the next case and hope for better results there. But we really need a better methodology than that. We need to know whether it is in general true in close call situations that the alternatives remain unconceived or whether they sometimes remain unconceived but in many cases are thought of but rejected for whatever reasons.

So my question concerns how to deal with cases where the record doesn’t substantiate the case as one involving unconceived alternatives. There are two possibilities that we need to be able to differentiate: one where there’s just no evidence about whether there are unconceived alternatives and the other where there is evidence that the alternatives are conceived. My worry is that every case will be categorized as the first sort if we don’t find evidence of unconceived alternatives. After all, what would a case have to look like for it to be a case where all “close” alternatives are conceived? We can describe what that would be in the abstract but with the vicissitudes of historical record, I doubt we’ll ever find such cases, but that’s no reason to think that there aren’t lots of them.

But perhaps Kyle doesn’t need a preponderance of cases in which unconceived alternatives remain. Perhaps all he needs is enough cases of that sort to undermine our confidence that there is a reliable connection between being a great scientist and having conceived of “close” alternatives. If that is all that is needed, Kyle’s job is easier, since it doesn’t take that many case studies to undermine our confidence in the reliability of this connection. There’s still a hint of a problem, but not as strong, since it is much easier to convince us that there aren’t enough gifted scientists than to convince us that most scientists are not gifted in this way. That is, we don’t need evidence for ungiftedness, we just need a defeater for giftedness.

So the moral of the story is this. Instead of describing the argument for denying realism by saying, “Scientists, even the very best, are not very good at conceiving of all the alternatives to their preferred theory, even when we restrict the alternatives to “close” ones,” the argument is more sympathetically interpreted as follows: for scientific realism to be sustained, we need a reliable connection between being a great scientist and conceiving of all the “close” alternatives, and there exist enough case studies of great scientists who simply lack this ability to cast legitimate doubt on the claim that we are justified in believing that our mature theories are true. So, we shouldn’t be scientific realists. The argument doesn’t need to strong thesis that scientists are not very good at conceiving of alternatives to their preferred theory, just that they are not good enough at it to sustain the epistemic thesis that we are justified in thinking that our present mature theories are true.


Comments

Unconceived Alternatives — 5 Comments

  1. Maybe I’m missing something, but isn’t it a big difference in favour of present-day science that the amount of scientist working in any area is much, much larger than it was in past times like Darwin’s? Every scientist may and will fail to concieve “close” alternatives to the presently accepted theories, but the scientific community as a whole will very likely think of all reasonable possibilities (reasonable given common background knowledge) if it is big enough. The particular failure of imagination that affects one scientist will not affect others, and vice versa.

  2. Alejandro, that’s an excellent point, and one that came up in discussion of Kyle’s paper (an objection raised by one of our impressive group of grad students!). Kyle granted the point, and if I remember correctly, rebutted the objection by pointing out the difficulties in confirming that the scientific community as a whole makes up for the deficiencies of the parts.

  3. Another point to consider, although not in and of itself a rebuttal to Alejandro’s point: not all scientists within a mature science are thinking of the same set of problems. That is, it isn’t as though we’ve turned loose a swarm of scientists on the same set of open problems from the 19th C but, rather, that the mature sciences have sub-divided into specialities, with new problems needing study and attention, and most scientists live and work in communities on one of these sub-branches.

    Put another way, a realist advancing a “more heads on the case” argument for realism needs to attend to the historical fact that the case, understood here as the set of problems worked by a mature science, itself has grown in cardinality over time. So, you’ve got two populations growing, scientists and open problems, rather than a fixed set of open problems and a growing number of scientists working on that set.

    Example: theory and practice of a speciality down on a branch of some tree (where most scientists live and work) might be radically reinterpreted by a re-think of a theoretical issue up near the root. Suppose, for instance, that some piece of (understandable) mathematics comes along to unify physics but it upends the ontological stories we’ve told about how to interpret the terms in the quantum domain and relativistic domain, respectively. It isn’t clear to me that a number of heads on the case argument for realism can easily reply to such a case.

  4. Is there any important difference here between there being concievable alternatives to a theory and there being particular famous scientists actually conceive of them? What I’m thinking of here is whether this argument against scientific realism (and I sort of like it it) isn’t simply that you can’t successfully refer to something that you can’t unsuccessfully refer to, and when it comes to scientific theories there is simply are no sufficiently elaborated alternatives to allow a scientist to fail by virtue of the “wrong theory”. It’s sort of a Kuhnian argument: all that really happens is that you identify your self as *not* a scientists–or another kind of scientists. But when working with theory, there’s just not question about “is he right about that now?” He isn’t conceivably wrong.

  5. Hey Certain Doubts Gang,

    I’ve just found time to respond to these posts on my Unconceived Alternatives argument, which I found interesting and useful–so thanks! I am a little worried that Jon has conceded too much on my behalf: notice that if we really think fundamental scientific theories are established by abduction or elimination of alternatives, it really should worry us that past scientists failed to conceive of alternatives that were far in the future and/or radically different from their own (e.g. Newton and quantum mechanics). I consider “nearby cases” or “close calls” only to undermine the plausibility of the _possible_ realist response that holds both (1) such failures of conception are _purely_ a product of the radically different theoretical context of contemporary science (cases like Darwin/Galton/Weismann show us instead that such failures routinely occur even among scientists working in (roughly) the same theoretical context in which the relevant unconceived alternatives would ultimately be recognized), AND (2) there is something special or privileged about the theoretical background of contemporary science such that we should not expect IT to change as inquiry proceeds in just the same ways we find for past science (=exceptionalism about present science). I do NOT concede that this sort of exceptionalism about contemporary science is plausible or compelling, and of course the realist would need to offer an independent argument in support of it in order to pursue this line of response.

    This makes a difference to Jon’s point about the inductive basis for the problem as well. It is only if the exceptionalist response has been made independently attractive or plausible that we need to worry about what the pattern of evidence for “close call” unconceived alternatives looks like: without the exceptionalism, the failure of Newton to conceive of QM (etc.) makes the evidence in favor of the general significance of the problem of unconceived alternatives look overwhelming. So what I need the historical record to show in addition is that such failures to conceive of alternatives (robustly attested to by the historical record in what Jon calls the “obvious” cases) aren’t an artefact of comparing the thinking of scientists working in radically different theoretical contexts or backgrounds (again supposing some privilege for the theoretical background of contemporary science can be made out). THIS is what the cases of Darwin, Galton, and Weismann are supposed to show. In what I think is the parlance favored by analytic epistemologists, I suppose I am defeating a potential defeater for the broad evidence base I already have (from the history of science), rather than seeking to found an inductive argument directly on cases just like the ones I consider (in which case I wouldn’t restrict myself to “close calls”, because I don’t think those are the only cases that matter). So Jon’s original concern about my methodology is, as he suggests, not such a problem, though not, I think, for quite for the reason he suggests. (Notice, for instance, that nothing here turns on claims about “giftedness” or a special role for “gifted” scientists, which I find worrying.)

    I find the subsequent comments equally intriguing, but let me restrict myself here to two remarks. First, Alejandro is absolutely right that the issue is ultimately what scientific communities can conceive of and not what individual scientists can: the latter issue is important only insofar as it bears evidentially on the former. The Darwin/Galton exchange is unusual in this respect, which is why in the Weismann case I present evidence that his contemporaries also failed to conceive of the alternative theoretical possibilities neglected by Weismann himself. (And of course the comparable failure of entire communities to conceive of alternatives that were _far_ in the future of a given scientific domain is a familiar feature of the history of science.) But in addition, we should not see even the Darwin/Galton case as one in which the scientific community effectively exhausted the well-confirmed theoretical possibilities: Galton conceived of _a_ common-cause alternative to Darwinian Pangenesis, but left many _other_ equally well-confirmed common-cause alternatives unconceived, including those that would prove most important to the course of future research.

    Second, wheeler makes an interesting point about the “more heads on the case” argument, but my own grounds for suspicion lie elsewhere. If we compare the institutions of contemporary scientific inquiry with those of the past, I find little reason to think that the number of heads on the case is the right thing to count. Galton, for instance, was an independently wealthy English gentleman conducting scientific research for his own interest and with his own reasons for challenging any number of the scientific orthodoxies of his own day. The professionalized structure of contemporary science, one might argue, offers far fewer incentives for innovation at the fundamental theoretical level than past science enjoyed: if you want to get it funded, for instance, your NSF or NIH grant application had better propose something new, but it had also better not be too far out of the mainstream with respect to its fundamental theoretical presuppositions. I am certainly not in a position to make a convincing case that the structure of contemporary scientific inquiry leaves us _less_ likely to discover previously unconceived alternatives than were the scientific communities of the past, but these considerations seem to me to dull the attractions of any simple appeal to the relatively larger number of heads we now have “on the case”.

    Thanks again to everyone for your useful and engaging input!

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