Beyond Positivism and Relativism: Theory, Method, and Evidence.
This is an account of the recent manoeuvres in Laudan's continuing defence of scientific rationality against the onslaught of the relativists. The latter are cast in the role of philosophical Visigoths - 'new crazies' who 'revel . . . in ambiguity and sloppy argument' (p. 3). Their chiefs are 'Kuhn, Feyerabend, the later Wittgenstein, the later Quine, the later Goodman, [and] Rorty' (p. 4). For the purpose of this review, it suffices to characterize their offending doctrine as the view that theory choice is unavoidably irrational (Laudan gives a fuller description on p. 5).
Two philosophical generations ago, the positivists were optimistically proposing various recipes for rational theory choice. These proposals invariably go into one or both of two sorts of trouble. First, there seemed to be no rational way for proponents of a given recipe to compel proponents of rival recipes to change their ways. Secondly, even among proponents of a given recipe, the choice of any theory T could always be challenged by showing that there are rival theories which satisfy the recipe just as well as T. The apparent intractability of these problems - the problem of justification and the problem of underdetermination - impelled the relativists of the following generation to conclude that theory choice is unavoidably irrational. It has fallen to Laudan to emphasize the weak spot in this line of thinking: the failure of the positivist recipes for resolving disagreements doesn't establish that there are no successful recipes to be found. It's possible that the failure was due to the constricting influence of unnecessary and unfortunate presuppositions. There's a logical space 'beyond positivism and relativism' for a position which concedes to the relativists that the positivists' enterprise was a failure, but which agrees with the positivists about the rationality of theory choice. In addition to opening up this space, Laudan has undertaken to furnish it with a diverse and highly original collection of non-positivist amenities.
I've selected three of Laudan's more central points for a detailed look. First, there's the infamous problem of incommensurability. When does a successor theory constitute an advance over its predecessor? The classical positivist criterion required that all the true claims of the predecessor be derivable from the successor. However, relativists argued that theories generally fail to be intertranslatable. This led them to conclude that there was no rational way to adjudicate disputes about the progressiveness of a theoretical change. Lauden counters this line of reasoning by proposing that there may be criteria of progressiveness which don't require intertranslatability. In particular, he proposes that 'science progresses just in case successive theories solve more problems than their predecessors' (p. 78).
Secondly, there's the equally infamous underdetermination of theory by all possible data. Problems of incommensurability aside, the putative fact that every theory has empirically equivalent rivals is supposed to undermine the rational basis for accepting any of them. In a chapter co-written with Jarrett Leplin, Lauden counters this threat in a variety of ways. One of them is by appealing to the fact that theories have empirical consequences only when conjoined with auxiliary hypotheses (p. 57). Since the permissible auxiliaries change with time as science develops, judgements of empirical equivalence can only be made relative to a given state of scientific opinion. Thus any pair of theories which are presently empirically equivalent may very well become empirically discriminable in some future state of science. Even if we're unable to choose between two empirically equivalent rivals at present, there's no basis for jumping to the conclusion that we will never be able to do so.
Thirdly, there's the problem of divergent methodologies. The arch-relativist Kuhn maintained that every paradigm carries with it its own methodological precepts for evaluating theories, and that each theory is judged to be superior to its rivals by the rules of its own paradigm. Lauden counters this with the claim that methodologies are themselves empirical hypotheses which are open to evaluation. They're conditional claims about the best way to solve certain kinds of problems in the sort of world that we happen to inhabit. The fact that methodologies can be evaluated means that they can be revised, and the fact that they can be revised means that two groups who start with different methodological principles may yet hope to agree in the end. This much of the story still leaves Laudan open to the charge of circularity - for doesn't the evaluation of methodologies require that we already have a methodology in place for conducting evaluations? Laudan's way out of the circle is to say that the evaluation of methodological efficacy depends only on knowing how to resolve 'low-level empirical claims' on which we all agree (p. 133).
In this dialectic between Laudan and the relativists, both sides take it for granted that possessing the resources for resolving disagreements is a necessary condition for rational schemes of opinion change. In each of the cases discussed above, the relativists point to a failure of this necessary condition, and in each case Laudan provides a remedy for the presumed failure. Almost all of the material in Laudan's book follows the same pattern. This is not a winning strategy - it's to play for a tie. At best, this approach might enable Laudan to show that scientists have the resources for arriving at agreement about any and all scientific issues. Such a result would discredit a particular type of argument for relativism. But it would not yet vanquish relativism itself. Possessing the resources for forging a consensus is, after all, only a necessary condition for rationality (if that). It's certainly not sufficient. It's possible that a universal consensus is within the reach of science, but that this is due to nothing more than a hard-wired cognitive bias.
Indeed, many of Laudan's arguments aim to establish an even weaker proposition. They don't show that agreement can be obtained in the contested field - they merely show that it hasn't been definitively demonstrated that agreement can't be obtained. For example, consider the argument about incommensurability. The relativists cite incommensurability as a reason for the irrationality of theory choice; Laudan says that problem-solving effectiveness provides a basis for theoretical comparison that doesn't depend on intertranslatability. But for the problem-solving criterion to elicit agreement, there has to be an agreed-upon manner of counting up problems. It's easy to imagine that the individuation of problems might vary from one paradigm to another, just as conceptual schemes do. Lauden doesn't provide us with a method for counting problems. He admits that his proposal is programmatic (p. 82) - that is to say, he merely notes the possibility of a problem-solving criterion that doesn't depend on intertranslatability. Maybe we'll be able to formulate such a criterion. But relativists can just as well speculate that we might not be able to do it. The burden of proof is equally distributed here. Even if Laudan's arguments are sound, he will have established no more than that his view of science competes on all fours with the relativist view. This limitation isn't explicitly denied by Laudan; but it's often disguised by a rhetoric which depicts the relativists as pathetic, vanquished foes.
There are some places where I think Laudan's analysis goes awry. For instance, it seems to me that the argument about underdetermination is mistaken. Let's grant that the permissible auxiliary hypotheses change with time, and that two theories which are empirically equivalent under the current auxiliaries may be empirically discriminable under the auxiliaries of future science. These concessions still aren't strong enough to de-fuse the relativist dilemma. For if every theoretical hypotheses has empirically equivalent rivals under the current auxiliaries (and this assertion isn't being challenged in this argument), then our total world-view - the conjunction of all the theoretical hypotheses which we're currently willing to accept - must also have empirically equivalent rival world-views. But world-views have their empirical consequences without the importation of any external auxiliary assumptions. Indeed, a world-view is formed by starting with any theory that we accept and conjoining it with all the auxiliary hypotheses which we deem to be permissible. Therefore empirically equivalent world-views are eternally empirically equivalent. Moreover, the argument from empirical equivalence to underdetermination isn't changed by running it with world-views rather than partial theories. I offer this criticism because Laudan and Leplin's argument from the 'instability of auxiliary assumptions' (p. 57) has been widely discussed. I don't think the point is crucial to Laudan's case, however, for he has several alternative means of combating the underdetermination argument. For instance, he denies the presumption that every theoretical hypothesis has empirically equivalent rivals in the first place, as well as the claim that empirical equivalence entails underdetermination. I happen to disagree with the first of these two denials; but the point isn't worth pursuing, since I agree with the second.
There's another, rather more significant problem with Laudan's analysis which arguably undermines large portions of his message. Consider the argument that different methodological assumptions lead to irreconcilably different theoretical preferences. According to Laudan, methodologies are conditional empirical hypotheses concerning the most effective way of achieving various cognitive ends; and methodological disputes can be resolved by appeal to 'low-level empirical claims' on which we all agree. These low-level claims are based on a straight-line enumerative inductive rule which Lauden dubs R1:
If actions of a particular sort, m, have consistently promoted certain cognitive ends, e, in the past, and rival actions, n, have failed to do so, then assume that future actions following the rule 'if your aim is e, you ought to do m' are more likely to promote those ends than actions based on the rule 'if your aim is e, you ought to do n' (p. 135).
This is a proposal which cries out for gruification. Suppose that actions of type m have promoted ends e in the past, and that actions of type n haven't. Then, supposing that our cognitive ends are e, rule R1 would seem to give us licence to prefer actions of type m. But let actions of type m' be defined as actions of type m if performed before today, and actions of type n if performed from today onward. Actions of type m' have been just as successful in promoting our cognitive ends as actions of type m. Thus R1 doesn't really tell us whether we should engage in actions of type m or actions of type n in the future. Our preference for actions of type m evidently depends on relatively high-level theoretical considerations. But, since theories are selected by methodologies, it isn't clear how an appeal to induction is going to ground our theoretical choices.
Laudan doesn't deal with the particular objection in his book. But his manner of extricating himself from kindred difficulties gives a clear indication of what he would say about it. In arguing that there's no algorithm for producing empirically equivalent rivals to any theory T, he briefly considers the putative rival [T.sup.*] which asserts that the empirical consequences of T are true but that the theoretical entities posited by T do not exist. [T.sup.*] is dismissed on the grounds that it fails to be a 'genuine rival' (p. 256). It is, in fact, a species of 'logico-semantic trickery' (p. 256). I expect that Laudan would say the same about the gruish methodological percept m' - it's just another logico-semantic trick. The argumentative function of this move is clear: it's to dismiss certain counterexamples to one's philosophical thesis on the grounds that they don't count. But what's the basis of this discounting? It seems to have something to do with whether or not a position has, or might have, serious advocates. Since Laudan's entire case depends on the elimination of these spurious rivals, it needs a rather more extensive discussion than it receives.
There is one place where Laudan gives us a further clue to his thinking on the subject. In trying to show that the ampliative rules of science don't universally underdetermine theory choice, he gives a historical example: the resolution of the debate between Newtonian and Cartesian physics. The ampliative principle in question is the following: when theories make conflicting and testable predictions, we should prefer the one whose predictions turn out to be correct. Now Newtonian and Cartesian physics made conflicting predictions about the shape of the earth, and both sides agreed that the results of careful measurement showed Newton to be right. QED. But what about the possibility that a Cartesian, subscribing to the same ampliative principle, might have denied the conclusion by challenging the accuracy of the measurements?
the advocates of strong ampliative underdetermination . . . will say, and quite rightly, that it would have been logically possible for the defenders of Cartesian physics to find some way post hoc of challenging the data . . . But . . . the fact that a course of action is logically possible does not create the slightest presumption that such a course of action is rational (p. 49).
As in the case of m' and [T.sup.*], we have a counterexample to a philosophical thesis dismissed on the grounds of irrelevance. The rationale for dismissal is that logical possibility doesn't entail rationality. Presumably, Laudan would say the same of m' and [T.sup.*]: both may be logically possible alternatives, but it doesn't follow that their espousal is a rational option. Note that Laudan's rationale doesn't fully warrant the dismissals. Even if it's true that logical possibility doesn't entail rationality, it certainly doesn't follow that these logical possibilities are irrational. But at least it creates a space for the type of dismissive manoeuver that he wants to engage in.
Or does it? I find the principle at stake to be singularly elusive. Taken at face value, the percept that logical possibility doesn't entail rationality knocks down a straw man. Of course, logical possibility doesn't entail rationality. After all, it's logically possible for someone to believe in contradictions. But this is not a thesis that defenders of m', or of [T.sup.*], or of the recalcitrant Cartesian's right to demur, have any interest in denying. In all three cases, the dismissed points of view have a lot more going for them than mere logical possibility. To begin with, they're also logically consistent. This doesn't yet get us very far, since the logical consistency of a belief still doesn't ensure its rationality. But m' and [T.sup.*] possess a virtue that goes beyond internal consistency: they satisfy the proposed rules of ampliation as well as m and T do. Why isn't that enough to conclude with the relativists that the ampliative rules in question don't favor m over m', or T over [T.sup.*]?
There are sporadic and undeveloped suggestions of two answers to the foregoing question in Laudan's text. Either or both of them may be what he really had in mind by the slogan that logical possibility doesn't entail rationality. First, he might be saying that m' and [T.sup.*] don't count because nobody has ever seriously adopted such views. The idea here is that the adequacy of a proposed ampliative rule depends only on its capacity to resolve real disputes between real opponents. Merely possible positions don't have to be worried about. This view has been endorsed by Ronald Giere, who, like Laudan, uses the discounting gambit to get rid of empirically equivalent rival theories:
Van Frassen's view is that we must choose one hypothesis out of a literally countless set of possible hypotheses. This looks to be a very difficult task given finite evidence and the logical underdetermination of our models by even their complete empirical substructures. I would urge a quite different picture . . . Looking at the scientific process, we see scientists struggling to come up with even one theoretical model that might account for phenomena which previous research has brought to light. In some cases, we may find two or three different types of models . . . These few models may be imagined to be a selection from a vast number of logical possibilities, but the actual choices faced by scientists involve only a very few candidates (Giere , pp. 86-7).
On this account, the rationality of science doesn't depend on our being able to resolve every sort of logically possible disagreement among proponents of the same ampliative rules. It's enough to be able to resolve the disagreements that actually occur. To be sure, [T.sup.*] is empirically equivalent to T, but scientists aren't at all interested in its candidacy (or else the recognition of empirically equivalent rivals wouldn't merely occur 'in some cases'). By the same token, nobody in the history of science has ever proposed a gruish methodological precept like m', nor would any informed scientist have been inclined to repudiate the painstaking geodesic measurements of the Academie des Sciences. Therefore these alternatives don't count.
It seems to me this proposal cannot be sustained. Suppose it's true that ampliative rules need only choose a winner from among the occupied positions - i.e. that it's always rational to adopt the best position from among those that are actually put forward. Then assassination would have to be considered a tool for rational decision-making. In order to establish that some methodology or theory should be adopted, we could follow a policy of judiciously doing away with all those whose thinking tends in the direction of promising rival hypotheses. By nipping potential rivals in the bud, we would be able to ensure the continued rationality of our favorite thesis. Conversely, a prankster could precipitate a scientific crisis by endorsing a gruish hypothesis just to make trouble. Once endorsed, the principle that only occupied positions count would be powerless to dispel it, unless we take the drastic and quite un-Laudanian step of making the rationality of a scientific decision depend on the motives of the parties involved. In fact, I hereby endorse all the m'- and [T.sup.*]-transforms of all the methodological rules m and theories T that are currently in play among scientists. Now what?
The second interpretation of the thesis that logical possibility doesn't entail rationality is based on Laudan's claim that ampliative rules needn't be algorithmic (pp. 17-19). Laudan needs to discount certain hypotheses even though they seem to satisfy all the requirements of the ampliative rules. An appeal to the non-algorithmicity of the rules might do the job by allowing us to say that a hypothesis can fail to satisfy a rule even if we can't stipulate exactly why it fails. In this case, the slogan 'logical possibility doesn't entail rationality' is interpreted to mean that there's a distinction between true conformity to a rule (rationality) and mere conformity to the letter of a rule (logical possibility). To be sure, this distinction isn't crystal-clear; but that's a problem for Laudan to worry about, not his critics. In any case, if we let the distinction stand, then there's the option of saying that while m' obeys the letter of the non-algorithmic rule for evaluating methodologies, it nevertheless fails to obey the rule.
A side-issue: when it suits his purpose, Lauden seems to demand algorithmicity just as much as any positivist. For instance, he criticizes David Bloor for claiming that the strong program in the sociology of science is 'scientific' even though Bloor admits that he 'cannot pinpoint or describe what the difference is between the scientific and the nonscientific, (p. 206). Lauden continues:
I have to say that this just won't do. If Bloor is to get the mileage he wants out of draping himself in the mantle of the scientist, he must indicate specifically and in detail what it is about his approach that makes it worthy of the label (p. 206).
That sounds like a demand for an algorithm for deciding what's scientific to me. If this kind of demand can be placed on Bloor, then we can just as well insist that if Laudan is to get the mileage that he wants out of discounting m', he has to be able to indicate 'specifically and in detail' what it is about m' that makes it susceptible to discounting.
Let's ask the following question about non-algorithmic rules: can people rationally disagree over their application? Is it possible for S1 and S2 to apply the same rule to the same information and get different results, or do different results indicate that at least one of them must have misapplied the rule? I'm not at all sure how one could tell which of these two states of affairs obtains. But set that problem aside. Suppose first that different people can obtain different results by the correct application of the rule. Then the rule underdetermines the result and Laudan's defence against relativism fails. Now suppose that the rule fully determines the result - everyone who applies it gets the same answer. In that case, the suggestion that the rule is non-algorithmic would seem to contradict Church's thesis. Now Church's thesis isn't engraved in stone; but one doesn't lightly make an enemy of it. At the very least, it has to be said that the idea of non-algorithmic rules needs more work.
More generally, the strategy whereby Laudan discounts apparent counterexamples to his views needs much more work. The slogan 'logical possibility doesn't entail rationality' won't bear the heavy philosophical load that it carries. This lacuna is, I think, the most important missing piece in Laudan's case for having provided a viable third alternative to positivism and relativism. But even if the missing piece is put in place, Laudan still won't have gained a tactical advantage over the relativists. He'll merely have shown that a particular argument against the rationality of theory choice doesn't work, thereby battling relativism to a draw.
Giere, R. N. : 'Constructive Realism', in P.M. Churchland and C. A. Hooker (eds), Images of Science, Chicago, University of Chicago Press, pp. 75-89.
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|Publication:||The British Journal for the Philosophy of Science|
|Article Type:||Book Review|
|Date:||Sep 1, 1997|
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