CHAPTER 5
LAKATOS AND LAUDAN ON PROBLEMS
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There have been two important attempts to improve on Kuhn's conception of science -- Lakatos' methodology of scientific research programmes and Laudan's account of science in terms of problem solving within research traditions.
Since I view Lakatos' account as a significant improvement on Kuhn's, I will present an overview of his entire methodology. However in the case of Laudan I will focus primarily on what he says about the nature of scientific problems and how they are weighted as to importance.
5.1 Lakatos' Methodology of Scientific Research Programmes
The major problems of a justificationist epistemology are: What are the infallible starting points for knowledge and how can we draw trustworthy inferences from them? In a non-foundationalist approach to knowledge, the above questions are shown to incorporate utopian presuppositions. Instead, knowledge is seen as being woven from many strands, any one of which may have to be replaced, and even the overall pattern will sometimes undergo major revisions.
However, if such an account of knowledge is to count as a genuine epistemology, it must provide some standards for criticism and revision. We want to say more than Feyerabend's iconoclastic motto that "Anything goes!" or Bridgman's inspiring but vacuous conclusion that "Scientific method is just using your head and doing your damnedest!"
Thus, for Popper, the central problem in epistemology became: Since all knowledge is conjectural, how can we criticize (and possibly improve) our conjectures? The core of Popper's solution is his theory of falsification, which says that conjectures are to be rejected if they are inconsistent with accepted 'basic' statements. Although some aspects of Popper's account of the empirical 'basis' of science are reminiscent of foundationalist accounts - often they describe medium-size observable objects about which it is easy to get intersubjective agreement - Popper emphasizes that his 'basic' statements are fallible (hence the ironic quotation marks), theory-laden, and attain their privileged status via methodological convention. By agreeing on singular existential claims, scientists are able to falsify universal explanatory theories.
Since Popper's 1934 Logik der Forschung, an enormous literature has developed concerning the exact nature of the fallible empirical base and the problem of the theoretical and social construction of facts. However, Lakatos, whose first philosophical interests were in logic and mathematics, focused on another problematic aspect of Popper's theory of falsification. Consider a case where the results of experiments are uncontroversial and clearly inconsistent with theoretical predictions. There remains a question as to exactly which premises in the theoretical system should be modified. Deductive logic dictates no choice and from his critical study of inductive logics, Lakatos expected no help from confirmation theory. Yet even a cursory glance at the history of science showed that scientists were not responding to falsifying instances in a random trial-and-error fashion.
Thus Lakatos argued that Popper's simple falsificationist theory of science should be replaced with a more sophisticated account, one which he called the methodology of scientific research programmes (MSRP). Later Lakatos also proposed a historical method of evaluating philosophical theories of scientific method - his so-called 'metacriterion'. I will discuss these contributions in turn.
a. Characterization of an RP
According to Lakatos, a research programme (RP) is a series of theories T1, T2... Tn where the theories must be related in two ways. First, they must all share certain core postulates (C) which by conventional fiat are not to be revised should the particular theory make false predictions. One of Lakatos' favorite examples of a hard core of a research programme consists of Newton's three laws of motion, plus the law of gravitation. An example of a theory within the Newtonian research programme would be Newton's treatment of the moon's orbit. Thus Newton's theory of the moon (call it T) consists of two parts - the core postulates (C) plus auxiliary hypotheses which provide a description or model of the moon-earth system (call it M).
Lakatos' second requirement on the theories in a research programme is that the auxiliary hypotheses which are attached to the core in order to make observable predictions must be generated by a positive heuristic (H), i.e., a more or less well-specified plan for modeling the world in increasing detail. Thus to pursue the above example, the heuristic of the Newtonian research programme would dictate not only that the model of the moon-earth system should include masses and distances (while omitting colors and chemical compositions), but would also indicate that as a first approximation point masses could be used. For a more realistic account, however, one might need to introduce an oblate model of the earth or include the influence of other bodies in the solar system.
Summing up. we may identify a research program with an ordered triple:
RP = <C, H, Tk>
where C is the set of core propositions and H is a function which starts with C and generates various models which when conjoined with C form the various constituent theories. Thus,
T1 = C + M1, where M1 =df H(C)
T2 = C + M2, where M2 =df H(C + H (C))
Tn = C + Mn, where Mn =df HN(C)
Note that H not only generates the first model M1, but also then operates on M1, to produce a more detailed model, M2. (Of course, in real scientific examples, at each step H would probably not generate a unique model, but rather a whole class of possible models, only one of which would be selected for testing.)
b. The Appraisal of Research Programmes
Having characterized a research programme, we can now turn to Lakatos' methodology of research programmes, i.e., his rules for how scientists should work with them. Lakatos' primary injunction is that scientists should honestly and publicly appraise research programmes. (It need not be irrational to work in a degenerating research programme, but it would be intellectually dishonest not to admit it!)
How then are RP's to be appraised? Lakatos describes a variety of evaluative factors; he does not attempt to provide a metric for aggregating them. A research programme is given a positive appraisal for:
a) Heuristic Power - having a strong positive heuristic which gives detailed advice about model construction for a wide variety of problems
b) Theoretical Progress - a research programme is theoretically progressive at stage n if Tn has more testable content then Tn-1. (As the models become more detailed, we can either predict more features of the system or make more precise predictions.)
c) Empirical Progress - a research programme is empirically progressive at stage n if any of Tn's additional testable consequences have been experimentally confirmed. (It does not matter if others have been refuted.)
A research programme is given a negative appraisal for:
a) Heuristic Degeneration - a weak or exhausted positive heuristic
b) Theoretical Degeneration - ad hoc theoretical development. (Lakatos distinguishes various senses of ad hoc, including both trial-and-error model building which is not guided by any heuristic plan and Popper's notion of ad hoc as reduction of testable content.)
c) Empirical Degeneration - none of the new predictions are confirmed.
The most surprising feature of Lakatos' theory of appraisal is his attitude towards prediction failures. There are no crucial experiments, no falsifications, and no crises brought on by the accumulation of anomalies. Any number of prediction failures can be tolerated as long as any theoretical or empirical progress is being made. Research programmes disappear because they are overtaken by more progressive ones, not because they are knocked out by the facts.
c. Methodological Advice
I have already mentioned that the direct implications of Lakatos' theory of appraisal for individual action are rather weak. As long as one admits to the present viscissitudes facing one's favorite programme, Lakatos would not dissuade one from working in it, i.e., from developing new theoretical models and testing them.
However, Lakatos does suggest that appraisals should guide social policy within the scientific community. He says that degenerating research programmes may properly be given low priority in funding decisions and scientists working in a failing programme may find it increasingly difficult to publish in good journals. In general, his theory of apppraisal places little value on purely empirical investigations which are not guided by a theoretical heuristic. It is on this basis that he devalues much of social science.
Lakatos also felt that his methodology of research programmes should provide the basic framework for all work in the history of science, whether it be the 'internal' history of ideas or the story of 'external' influences on science. I will discuss this historiographic programme in a later section which deals with his theory of the metacriterion.
d. Analysis of the MSRP
Since Lakatos' methodology was deliberately designed to overcome inadequacies in Popper's account, the logical first step in trying to understand Lakatos' MSRP is by comparing it to Popper's falsificationist methodology.
Popper realized the logical ambiguity of falsification and discusses the holistic views of Duhem and Quine: "Now it has to be admitted that we can often test only a large chunk of a theoretical system, and ... it is sheer guesswork which of its ingredients should be held responsible for any falsification." (p. 239) However, he felt that the so-called 'Duhemian problem' was not always insurmountable. Often logical analysis can help localize the source of the prediction failure. And if certain parts of the theoretical system have gained striking empirical corroboration, perhaps by successfully predicting new effects, they will tend to be retained:
"...it is only through these temporary successes of our theories that we can be reasonably successful in attributing our refutaitons to definite portions of the theoretical maze."
However, Lakatos found this solution unacceptable for two reasons. First, as Agassi had already pointed out, the idea of retaining certain premises because they were well corroborated, had a "whiff of verification" about it which was inconsistent with Popper's own critiques of inductive logic. Secondly, and more importantly, Lakatos believed that most actual theoretical systems began life in an "ocean of anomalies." Hence, the core of a new research programme would never be able to gain enough corroboration to protect it from Popperian falsification.
The MSRP offered another solution to the Duhemian dilemma, one which depended on the idea of a crucial experiment, although with quite a different twist from the way in which Popper had conceived of it. Lakatos' solution worked as follows. Consider two successive theories in a research programme, Ti and Tj. These will differ only in their physical models, Mi and Mj. Suppose Ti leads to a prediction failure but Tj is successful. Then by a sort of higher level application of Mill's method of difference, we may decide to blame Mi for Ti's false prediction instead of the core C. So although Lakatos' rhetoric stresses confirmations over refutations, the basic logic of his methodology is indeed a falsificationist one and corroboration plays less of a role in his system than it did in Popper's!
This does not mean that Popper would or should accept MSRP as a friendly amendment. Popper's motto of "revolution in permanence" and his criticisms of Kuhnian normal science are incompatible with Lakatos' willingness to decide beforehand to stick to the hardcore of a programme for an indefinite period of time. On his account models of particular situations are under constant revision but there is no straightforward and direct method of subjecting the core to critical scrutiny. We can easily correct our little mistakes in modeling, but we may be stuck with erroneous big core assumptions indefinitely. If Lakatos is right in saying that scientific research programmes cannot be refuted, both by convention and for logical reasons due to the imperfect nature of the modeling procedure, then Popper's famous demarcation between falsibiable science and unfalsifiable metaphysics dissolves. The difference between Einstein and Freud becomes one of degree, a question of comparing the progressive-ness of each of their research programmes. As Lakatos puts it, on his account there is no "instant rationality."
The above analysis immediately suggests some of the philosophical criticisms which have been made of the MSRP. But before turning to these, let us first look at Lakatos' theory of historiography because he felt that the most cogent way to evaluate the MSRP was through the history of science.
5.2 Lakatos' Metacriterion
When logical positivists and empiricists talked about science, it was clearly in the prescriptive mode. An axiomatization of a mature scientific theory was an unabashed attempt to display the basic logical and epistemological features of the theory. A good theory of confirmation would specify how scientists should reason inductively. If in practice scientists blurred the analytic-synthetic distinction, or failed to distinguish clearly between theoretical and observational terms, or had incoherent subjective probabilities, so much the worse for them. Philosophy of science was prescriptive, not descriptive.
But beginning with Popper and Hanson, philosophers began to supplement their logical arguments with references to the actual practice of scientists. And Kuhn in his 1962 Structure of Scientific Revolutions not only plead guilty to producing a theoretical blending of the previous distinct contexts of discovery and justification, but also called for a naturalistic appraisal of logical-epistemological accounts, saying that they should be subject to: "...the same scrutiny regularly applied to theories in other fields. If they are to have more than pure abstraction as their content, then that content must be discovered by observing them in application to the data they are meant to elucidate. How could history of science fail to be a source of phenomena to which theories about knowledge may legitimately be asked to apply?"
However, neither Kuhn nor other early members of the historical school of philosophy of science made it very clear exactly how the data of history should interact with the in theories of philosophy. It is here that we find Lakatos making a second major contribution to the philosophy of science in his "History of Science and its Rational Reconstructions".
a. How Philosophy Informs History of Science
The paper in which Lakatos proposes that a Historiographic Research Programme be used to appraise his Methodology of Scientific Research Programmes begins with echos of Kant: "Philosophy of science without history of science is empty; history of science without philosophy of science is blind." The pattern of argument is dense with dialectical and self-reflexive manoeuvers, interspersed with Lakatosian jokes and rhetorical flourishes. What I have attempted to do here is to present a simplified summary of Lakatos' basic position which the reader may wish to use as a guide to the original paper.
Let us begin with the influence of philosophy of science on history of science. As realists we should sharply distinguish between history as past events (what Lakatos calls "actual history") and history as a narrative about actual history (which I will call "written history"). Lakatos' first claim is that philosophy of science has little influence on actual history. Unlike Laudan, Lakatos believes that while contemporary philosophical methodologies may influence a scientist's rhetoric (causing Newton to claim that he doesn't feign hypotheses), they have negligible effect on basic scientific practice, how scientists appraise claims, design experiments, etc. We might draw an analogy with the minimal influence of formal logics on the patterns of argument actually used by systematic thinkers. Thus Euclid's reasoning was much richer than the syllogistic logic of his time, although he sometimes attempted to force it into syllogistic form.
There is a sort of essentialism in Lakatos' position here. At the very least he believes that the implicit rules governing scientific practice are relatively invariant. Furthermore, they are much more sophisticated than any philosophical theory of methodology put forth to date.
The situation is quite different when we turn to written history of science. In this case Lakatos believes that some theory about the growth of science must be used to structure the historian's account. Agassi had demonstrated in his 1963 monograph that for each philosophical theory of science, e.g., inductivism, conventionalism, falsificationism, there was a corresponding historiographic approach. Thus in discussing the phlogiston theory, an inductivist historian would claim that the theory was a non-starter, a deviation from the path of true discovery from the very beginning; a conventionalist would emphasize what an economical conceptual scheme it provided for classifying diverse chemical reactions; a falsificationist would talk about its predictive power, followed eventually by a refutation at the hands of Lavoisier.
As Lakatos pointed out, every philosophy of science proposes a normative account of what scientists should be doing. When scientists actually behave in a rational fashion [modulo a given methodology], then that behavior requires no detailed explanation and the story of that rational practice is what Lakatos calls "internal" history. Any behavior which is not in accordance with a particular methodology is ruled non-rational [modulo that methodology] and deviations from rational practice must be explained in terms of factors external to the methodology, in what Lakatos calls "external" history.
Lakatos emphasizes that each philosophy draws the internal/external line differently. Thus, to pursue our example, the inductivist has to produce an external explanation as to why the phlogistonists theorized so far beyond observable data, while the falsificationist need only give an explanation of any ad hoc adjustments of the theory - it is taken as given that scientists will make bold conjectures.
In order to dramatize this important distinction between internal/external history, Lakatos introduces his controversial concept of "rationally reconstructed history" and even goes so far as to suggest that historians should put the rationally reconstructed version of events in the main body of the text, while relegating the story of what actually happened to the footnotes! Not surprisingly, Lakatos' critics, especially professional historians, have had a field day with this proposal, which sounds suspiciously like an endorsement of ideologically motivated fabrications of history.
However, I think the main thrust of Lakatos' proposal is not so far-fetched; granted his stylistic suggestions as to what should go in the footnotes are ill-advised. In physics it is common practice to first present an idealized account of a pendulum, lever, orbit, or trajectory and then to go on to explain away departures from ideality in terms of external influences such as friction or air resistance. Linguists use a somewhat similar strategy when they distinguish competence from performance. When the speaker is tired, pressed for time, or distracted she is apt to make utterances which she in some sense knows to be incorrect.
Any account which is intended to explain the effects of perturbations must first present the idealized, non-perturbed situation to be used as a baseline against which one can compare the more complicated, messy actual situation. This is exactly the function of Lakatos' rationally reconstructed historical episodes. By 'subtracting' what a competent scientist would have done from what actually happened, we can isolate the perturbations in performance which require external explanations. Where Lakatos and the historians probably really do disagree is in their predictions about how frequently 'footnotes' will be required and how long they will be. At least in the case of physical science, Lakatos thinks that the historical story will be largely an internal one - if we choose the correct methodology as our normative theory. We now turn to a discussion of how that choice should be made.
b. How History Informs Philosophy of Science
According to Lakatos, each normative theory of scientific method defines a different internal/external demarcation for the historian of science and will hence dictate different rational reconstructions of past episodes. Given this plethora of written histories, how can we possibly use them to choose between methodologies?
Lakatos provides two answers:
a) we should prefer that philosophical theory which renders more of the actual history as rational - i.e., which provides the most complete internal account and leaves the least number of events to be explained by external factors. I will call this the Maximal Coverage criterion.
b) Lakatos also says that we should prefer the philosophical theory whose accompanying historiographic research programme leads to the discovery of the most novel historical facts. Let us call this the Novel Facts criterion.
An illustration of how these criteria are supposed to operate is provided by John Worrall's careful case study of the impact of Young's famous interference experiment. Why, asks Worrall, did Young's 'crucial' experiment not lead to an immediate abandonment of the corpuscular theory of light? On a falsificationist account, this tenacity would have to be explained by external factors, such as Newton worship, the obscurity of Young's paper, or academic politics. Worrall digs up new historical evidence which undermines each such proposal. He then argues that at the time of Young's experiment, the corpuscularian research programme (in part because of its strong heuristic) was more progressive than the wave approach and so according to the MSRP, Young's contemporaries were behaving perfectly rationally in not taking the experiment to be a refutation. Worrall also produces quotations which show that early 19th century scientists were aware of their Lakatosian reasons for downplaying Young's results until the wave programme became more progressive.
Worrall's history, which is based on the MSRP, reconstructs more of the actual past as rational. Furthermore, it correctly predicts many of the scientists' stated evaluations of the situation. Thus on Lakatos' metacriterion, this historical episode should count in favor of his philosophical methodology.
c. The Issue of Circularity
According to Lakatos' methodology of scientific research programmes, the scientific community should prefer that scientific approach which is most progressive in its heuristic, theoretical and empirical dimensions. According to his metamethodology of historiographic research programmes, the philosophical community should prefer that scientific methodology which is most progressive in historical research. Thus Lakatos' metaproposal for evaluating competing scientific methodologies incorporates the very same principle which underlies his own preferred scientific methodology. How can this be fair?
Lakatos presents the following ingenious argument on behalf of his metacriterion. Let each competing scientific methodology generate its own parallel historiographic metacriterion. For example, let's evaluate inductivism inductively. Does the history of science offer strong inductive support inductivism? Clearly not - naughty scientists are constantly feigning hypotheses and making bold conjectures. Similarly falsificationism is falsified by the history of science, e.g., by the Young episode. And conventionalism does not give the most economical account of scientific activity (so Lakatos claims).
Thus since every other scientific methodology fails according to its own metacriterion, the competitors have nothing to lose by submitting to Lakatos' metacriterion. And in principle they could even turn out to be more progressive on the Lakatosian metacriterion. If there were no hardcores in the history of science or if scientists generally acted like Popperians or Baconians or Duhemians, then the MSRP would not triumph in the historiographic domain. So adopting a particular research programme's metacriterion does not guarantee the selection of that same research programme's methodology for science.
However, a critic might grant that the MSRP provides the best description of certain behavioral norms of the scientific community but deny that this fact makes it the best methodology. (This would be like arguing that nepotism must be a component of good government because it is found in most societies.) Such a critic would insist that the metaevaluation be done using traditional philosophical analyses, instead of any sort of naturalistic appraisal.
Lakatos has two replies to this objection. First, he points out that aprioristic arguments have yet to yield a philosophical consensus and maybe his metacriterion will. Secondly, philosophers of science admit that science is the most successful way of generating knowledge that we have. Is it not then hubris for the philosopher to use armchair arguments as a basis for trying to tell scientists how to behave more rationally? (This would be like trying to insist that mathematicians use only the syllogism or propositional calculus when they construct proofs.) Of course, if science should suddenly undergo a Lysenko-type decline then the philosopher of science who had humbly extracted a methodology from naturalistic sutudies of great science might then be in a position to regiment scientific practice.
5.3 Reactions to Lakatos' Account
I have endeavored to give a sympathetic summary of Lakatos' scientific methodology and his historiographic approach. By necessity, my account is simplified in many ways, especially in its omissions of Lakatos' pioneering work on the growth of mathematics which introduces a theory of conceptual change and his critique of inductive logic where he clarifies his notion of degenerating problemshift. Both of these areas of research contribute to our understanding of his philosophy of science. In trying to first present Lakatos' views in as positive a light as possible (we will turn to criticisms in the next section), at some points I may have inadvertently projected backwards onto Lakatos' essays clarifications and perhaps even modifications of his views which are really contributions of Lakatos' students and colleagues. It is to these friendly amendments that I now turn.
Although Lakatos urges us to distinguish carefully between external and internal aspects of the growth of knowledge, I find it very difficult to do so in the case of the reception of Lakatos' philosophy of science. The history of the philosophical community (or better, communities) in this period has yet to be written but it would surely have to include diverse factors such as the following - their relative weights are less clear.
At the 1965 conference in Bedford which resulted in four volumes edited by Lakatos Kuhn's 'discovery' of normal science was seen as a challenge to Popper's falsificationist methodology and the MSRP was offered as a reply. Furthermore, Lakatos' historiographic theory sounded a clarion call for historical case studies and gave explicit guidance as to how they should be structured, thus providing ideal topics for Ph.D. theses or long papers. In addition, Lakatos provided various forums for the presentation of results. After Popper's retirement, he took an active role in the programming for the famous "Popper Seminar" at the London School of Economics. Lakatos planned the 1974 Napflion Conference, which resulted in two volumes of case studies. And he was one of the originators of the 1975 Kronberg conference which provided a variety of philosophical critiques of his approach. Lakatos' untimely death shortly before the Napflion Conference lent a certain poignancy to all these discussions and led to the publication of yet a third collection of essays, a memorial volume edited by Cohen. As a result of all these factors and others, Lakatos' work received a great deal of discussion and critical scrutiny. Let us now survey some of the dominant themes which emerged.
a. Status of the 'Hard Core'
On Lakatos' account the core postulates of a RP remain invariant over the life of the research programme because of a methodological decision made at the beginning. But case studies cast a variety of doubts on the historical adequacy of this claim. Musgrave argued that even in Lakatos' favorite example, Newtonian mechanics, scientists explored variants of the law of gravitaiton so the core was not given uncritical acceptance. And in many examples, the 'core' (to the extent one existed) was assembled piece-meal and/or underwent modification during the life of the RP - for example, the basic properties assigned to caloric, or phlogiston, or Daltonian atoms, or Newtonian light corpuscles kept changing as scientists tried to accomodate more and more phenomena. Various responses are open to a Lakatosian - one might 'soften' the core or move to a cluster concept, but then there may be problems of individuating RP's. The distinction between a core (which should be relatively invariant) and models or auxiliaries (which are constantly being tinkered with) now becomes fuzzy.
A second strategy would be to include within the core only those postulates which were non-controversial and unchanging over long periods of time. But now there is the danger that the true core of a programme (on this strict definition) would be as bland and non-distinctive as Aristotle's common axioms. For example, in attempting to formulate a definition of 'Darwinian' for a study of 19th century biology, David Hull found that there was no single basic tenet which Darwin, Huxley, and Wallace all agreed upon! (It should be noted that although Kuhn's concept of 'paradigm' is notorously vague, he is less vulnerable to the attack of mutability because he allows for the 'articulation' of the paradigm, e.g., development of the core theoretical structure. And since 'exemplars' are not given precise propositional descriptions, scientists are at liberty to give them varying interpretations.)
A third response, and perhaps the most likely one, is to cheerfully admit that the Lakatosian concept of RP is an idealization, one which will help us make sense of history, but will not fit it perfectly.
b. Nature of the Positive Heuristic
One of the most innovative aspects of the MSRP was its emphasis on heuristic principles as vital constituents of a RP that played an essential role in its evaluation. A strong heuristic could earn an RP plus marks even in the absence of empirical success, while predictative success stemming from ad hoc or trial-and-error tinkering with a theory added nothing to the positive appraisal of a RP. Unlike the core, Lakatos knew from the beginning that the positive heuristic of a RP might be somewhat vague.
The historical case studies revealed a great diversity of ideas which might count as positive heuristics of an RP, ranging all the way from the hodge podge of different techniques for purifying chemicals which a defender of Prout's hypothesis might invoke to explain why a certain atomic weight wasn't a whole number to the elegant methods of analyzing the symmetry properties of molecules which guide the choice of Hamiltonian for calculations in quantum mechanics.
This rich diversity of instances of positive heuristics raises the question of exactly how we are supposed to measure or compare the heuristic 'strength' of competing RP's. The vagueness of some heuristics also suggests that it may often be difficult to tell whether a particular theoretical innovation was 'guided' by a given positive heuristic, where the desired relationship is to be an objective one, not a mere psychological association. Urbach takes up the problem of how a heuristic is to be evaluated, proposing that heuristic power be assessed along at least three dimensions, which he calls precision, resourcefulness and autonomy. It might also be possible to incorporate much of the recent philosophical work and computer simulation studies of scientific discovery into a Lakatosian framework.
Yet, here again, there is a fundamental tension in the MSRP. Lakatos values powerful heuristics, but a really strong heuristic will place severe limitations on possible models. Suppose the heuristic of some program says there are only three possible models. In such an extreme case, the entire research program consists of only three theories:
RP = T1 v T2 v T3
where
T1 = C + M1, etc.
in which case all variants of the RP might quickly be refuted in a Popperian fashion and Lakatos' logical point about the impossibility of falsification disappears.
However, in the other extreme case where the positive heuristic puts very few restrictions on the class of possible auxiliary hypotheses, then theoretical progress will be too easy to come by because all sorts of ad hoc tinkerings will be compatible with the heuristic and the program will never degenerate.
c. The Problem of the Novelty Requirement
In reaction to the instrumentalist project of merely "saving the phenomena", realists have always dreamt of "anticipating Nature". Bacon believed that by following his method it would be possible not only to understand hidden natural processes but also to produce useful new technologies. Many philosophers have taken the ability of a scientific system to predict the existence of hitherto unknown effects to be an important epistemological indicator. Thus Popper says a theory's degree of corroboration is dramaticity increased when it correctly predicts a surprising result, i.e., a type of event which is quite improbable on background knowledge. Lakatos also introduces a novelty requirement, saying that a progressive RP will tend to generate novel facts while its degenerating rivals will be constantly trying to come up with post hoc explanations for these new phenomena.
But it is unclear in both Popper and Lakatos exactly how "novel" is to be understood. If they mean temporal novelty, then we would have to say that Newtonian mechanics should receive lots of credit for predicting the return of Halley's comet but none for explaining the tides because tidal phenomena were hardly surprising and the explanation was temporally post hoc.
Zahar argues that because of its stress on heuristics, the MSRP can explicate the role of novelty in a way not available to Popper. Zahar suggests that a fact is genuinely supportive of a theory if it was not used in the heuristic reasoning used by the scientist while arriving at the new theory. If the fact is temporally novel this requirement will automatically be satisfied. Otherwise it will be necessary to delve into the scientist's notebooks to discover the route pursued.
Worrall modifies Zahar's proposal so that it sounds less subjective, saying that whether a fact supports a theory depends on the objective relationships between fact, theory and the heuristic of the research programme. The problem of novelty is still very much of a contested issue. See, for example, Worrall's later, more detailed account and Howson's criticisms from a Bayesian perspective. Let us now survey some of the less sympathetic responses to Lakatos' philosophy.
5.4 Radical Criticisms of Lakatos' Approach
Both Lakatos' methodology and his metacriterion have been severely criticized. Since the attacks come from such a wide variety of competing philosophical stances, ranging from epistemological anarchism to positivism, it would obviously be impossible in principle to modify his doctrines so as to satisfy everyone. I will now summarize some of these criticisms, trying for now to leave it up to the reader to decide how telling each one is, although some of my own evaluations may peek through. I will then give a brief account of my overall assessment of the situation in a concluding section.
a. Methodological Anarchism
In discussing Priestley's refusal to abandon phlogiston theory, Kuhn suggests that it may be psychologically impossible for some scientists to make the Gestalt switch necessary to adopt a new, more promising paradigm. Lakatos, however, argues that there are never compelling epistemological reasons for switching research programmes, although there may be prudential ones, such as the availability of funding. No matter how badly an RP has degenerated, it is possible that it may make a come-back.
Various critics have argued that this makes Lakatos' methodology vacuous since it rules out nothing. In protesting against the "Popperian thought-police",
Lakatos' position prevents us from saying that in the 20th century it is irrational to pursue Velikovsky's research programme, Creation "Science", or phlogistic chemistry. All we can do is to point out that they have been degenerating for a long time. Furthermore, the argument would go, Musgrave's amendment saying that the MSRP does allow us to give advice to the scientific community about how to allocate its resources, is still too weak. There is a difference between betting on a long-shot and betting on a horse which is not even in the race!
b. Sociological Naivete'
According to Lakatos, any rational judgments made by scientists (i.e., judgments made in accordance with the MSRP) require no explanation. It is only the deviations from rationality which must be accounted for. This asymmetric attitude towards the problematizing of behavior is fairly common. We generally don't ask how a scientist was able to make a correct observation report or to argue validly or to maximize expected utility. But we often go to great lengths to explain the source of erroneous lab reports, fallacious reasoning, or incoherent probability assignments.
However, this strategy is really an unfortunate remnant of Aristotelian essentialism - if man is by nature a rational animal, there's nothing more to be said. But whatever rationality there is in science must presumably be fought for and internal history is just as deserving of analysis as is external history.
For example, how is the consensus around 'basic' statements negotiated? How are hardcores agreed upon? Let us grant for a moment that the MSRP correctly describes the norms of science. We must still ask how these norms are learned, internalized, and transmitted over time, space, and cultural bouindaries. Or does Lakatos believe his methodology is part of the deep structure of the human mind? But if that is the case, in what sense does his account describe something distinctive about science? It is not enough to discuss scientific norms in the abstract without looking at the scientific institutions in which they are embedded. Neither is it possible to understand deviant scientific behavior without knowing how the norms are enforced.
Those critics who think there can be no adequate philosophy of science without a sociology of science would take the argument a step further and deny that there are any invariant methodological standards, so the question of the correctness of the MSRP does not even arise.
c. Neglect of Historical Changes in Practice
In most respects Lakatos is very sympathetic towards the assumption of an historical perspective. To appraise a research programme we must look at how it developed over time. Were the successive theories generated by a positive heuristic? Is there a general pattern of improvement or is it now degenerating? To appraise a philosophical methodology, we must look at how scientists in the past evaluated the scientific proposals of their era. We are supposed to prefer that methodology which reconstructs most practice as rational (as defined by the methodology), where our domain consists of about four centuries of science.
But is it really plausible to believe that during that entire period there were no changes in methodology? There have certainly been many variations in the official philosophies of science. Compare, for example, the criteria for publication/rejection of the journals run by the early Royal Society with those catering to the Naturphilosophen. Or compare the methodological doctrines of behaviorists with those of transformational grammarians. Or consider the evolution of scientists' theories about how to report and deal with experimental error.
Given this variation, exactly which parts of past science should our methodology attempt to capture? Only the most recent? And what right have we to project the norms of the MSRP or any description of past practice onto future scientists? This is unacceptably conservative. Debates about the mutability of methodological norms have been inconclusive, partly because of lack of agreement about what exactly is to be designated by the term. If we give a rich, detailed account of scientific methodology, then it is constantly developing. If we choose a more abstract and general description, its principles are more widely agreed upon, but they now seem to be less characteristic of science per se, as is indicated by the very fact that Lakatos' historiographic theory at the meta-level is an exact parallel of his philosophical theory of science!
d. Dogmatic Decisions
Popper argued that rationality was based on criticism, not on justification. While giving up the positivists' methodological approach to science, he retained their concern for epistemological respionsibility and so he proposed various ways in which scientists could maximize criticism. Conjectures should be highly falsifiable; the tests conducted should be severe; scientists should not employ conventionalist strategyms.
Lakatos felt that Popper's approach was unworkable and proposed the MSRP in its place. But many critics have argued that in so doing Lakatos has blunted the various Popperian modes of criticism to such an extent that his methodology, if implemented would destroy the rationality of the scientific enterprise. Many of the complaints stem from Lakatos' discussion of the hard core. Lakatos claims that the best way to solve the Duhemian problem is to extend the conventional status which Popper awards singular 'basic' statements so that it also attaches to the most fundamental theoretical generalizations. By so doing, when predictions fail we can unambiguously direct the arrow of modus tollens towards the 'protective belt' of auxiliary hypotheses.
But there are vast differences in the conventional status of these two classes of statements. It is extremely easy to generate wide consensus about 'basic' statements while in the case of hard cores, there are typically rival research programmes. Secondly, Popper says that if anyone can offer a specific criticism of a basic statement (not just a general sceptical objection), then the statement immediately loses its preferred status. Lakatosian hard cores, by contrast, are declared invulnerable to refutation.
This dogmatic stance has led to a variety of criticisms. Koertge argues that in some cases hardcores can be criticized directly without making question-begging assumptions about the truth of auxiliary hypotheses. An example would be the logical inconsistency between the core assumptions of Aristotlelian physics and Copernican astronomy which could never be patched up by fiddling around with auxiliaries - one of them had to go.
Lakatos' MSRP has no parallel to a Kuhnian crisis which is brought on by repeated failures. However, Bayesian analyses have been used to argue that although the prediction failures may at first have a larger impact on the probability of the auxiliary hypothesis than it does on that of the core postulates nevertheless after a long period of degeneration we come to a crossover point at which time it would become rational to change the hard core rather than the protective belt. Thus there may be internal reasons for abandoning a research programme even in the absence of a more progressive rival.
Since Lakatos does not analyze the conventional decision concerning the hardcore, he does not realize that the factors which lead us to adopt a research programme in the first place may be quite different from those which would dictate the decision to reject it or keep it later on. Koertge provides a decision-theoretic analysis of two different responses by Mendeleev to refutations of the Periodic Table and suggests that we always need to consider a variety of factors, including heuristic power, the availability of alternative hypotheses, and empirical success. Laudan argues that we should clearly distinguish between the 'logic of acceptance' and the 'logic of pursuit'.
All of these criticisms point to the same conclusion: the methodological and epistemological status of the so-called 'hard core' will change dramatically during the life of a research programme. It cannot be taken as an unproblematic 'given', as Lakatos would have us do, without seriously undermining the rationality of science.
5.5 General Evaluation of the MSRP
Lakatos began his philosophical research with a concerted attack on Kuhn's psychologism. He hated the idea that scientists were victims of a band-wagon mentality which made them incapable of viewing the world from the perspective of an alternative metaphysics until they suffered a crisis-induced, collective nervous breakdown and converted to a new paradigm. Yet he also believed that Kuhn had described important features of the growth of science which were missing from Popper's account. So in a sense Lakatos set out to "Popperize" Kuhn. He wanted to give a theory of scientific methodology which would exhibit the rational, objective aspects of scientific inquiry. Discovery was to be depsychologized and seen as dependent on heuristic plans which in principle could be written down and discussed. Research programmes were to be appraised by objective criteria of progress or degeneration. But Lakatos was also keenly aware that an appeal to objective standards can easily be perverted into a weapon of totalitarianism. He repeatedly stressed the fallibility and incompleteness of methodological appraisals and said they could not be used to cast aspersions of irrationality on non-conforming scientists. For Lakatos there was no 'instant rationality' - the evaluation of a research programme was a long and tentative process.
Philosophical responses to Lakatos have been varied. Laudan has proposed a theory of research traditions which veers off more in the direction of Kuhn - explanatory problems arise from psycholgical puzzlement and truth plays no regulatory role in his system. Andersson on the other hand tries to show that Popper's critical rationalism can provide an answer to the objections posed by Kuhn, Lakatos and Feyerbend. Worrall's forthcoming book promises to develop and defend Lakatos' general approach against various criticisms.
My own view is that the theory of rationality contained in Lakatos' methodology of scientific research programmes is too weak, especially if it is viewed as a regulative ideal for scientific inquiry, not as a description of past compromises. But Lakatos did succeed in opening up some new areas of philosophical inquiry which have turned out to be very fruitful. To propose an historiographic research programme as a criterion for philosophy was too strong but it does provide one additional method for criticizing methodological theories. It has also produced some very interesting history of science. And the reflexivity incorporated into Lakatos' metacriterion is much more sophisticated than many of the naive naturalistic approaches which are popular today, especially amongst evolutionary epistemologists.
Perhaps the most exciting aspect of Lakatos' philosophy was its emphasis on heuristics. In a 1965 lecture, Post had argued that there were objective guidelines for the construction of new theories. Kuhn had talked about the perceived puzzle solving power of paradigms. But Lakatos was the first to consider heuristics to be a central component of science. Lakatosian research programmes have two equally important constituents, a core and a positive heuristic. The heuristic enters not only into the appraisal of the promise of the programme, but also into the accessment of its degree of empirical support. Nothing remains of the old discovery/justification dichotomy.
Following Lakatos, it will be difficult for any philosophy of science to ignore either history or heuristics. And that is a great achievement. Let us now turn to his remarks on problems.
5.6 Lakatos and Problem Shifts
Popper and Kuhn each highlight the kind of problem they think is most important. In Lakatos we have the beginnings of a more detailed theory of evaluation -- it centers on his concepts of progressive vs. degenerating problem shifts. Lakatos was very conscious of the interaction between methodologies on the object and meta-levels. If we compare the methods displayed in his own work as philosopher, historian or politician with the methods prescribed for or attributed to science and mathematics, we will find remarkable consiliences. The man who described the "concept stretching" of mathematicians studying polyhedra was also very adept at stretching Popper's concept of falsification until it included his own confirmation-based methodology of scientific research programs! [See NK] The problem of when and how concepts should be modified is an important one, but our concern here is with the issue of how and when problems should be shifted.
Lakatos' first major philosophical paper in English was "Proofs and Refutations." The edited version published after his death bears the sub-title "The Logic of Mathematical Discovery." The implied parallel with Popper's L.S.D. is an apt one, for what Lakatos does is to carry Popper's anti-justificationist critique of traditional philosophy of science over into the realm of mathematics. He argues that the Euclidean formalist account of mathematics which sees it as an ever increasing series of conclusively proved theorems derived from crystal clear axioms is at odds with the actual history of mathematics which is informal and conjectural and which grows through the criticism of proofs and drastic reinterpretations of concepts.
Lakatos repeatedly cites Polya and Popper as intellectual influences and around the L.S.E. in the sixties we always assumed that the teacher in the essay (which is presented as a dialogue) was modelled on Popper's own classroom performance. Certainly the following excerpt which ends one section of his essay sounded all too familiar to us:
"TEACHER: ... Let us close our discussion for the
time being; we shall discuss this new stage some other
time.
SIGMA: But then nothing is settled. We can't
stop now.
TEACHER: I sympathize. This latest stage will
have important feedback to our discussion. But a
scientific inquiry `begins and ends with problems.'
[Leaves the classroom.]
BETA: But I had no problems at the beginning!
And now I have nothing but problems!" (PR, p. 105).
"Proofs and Refutations" contains many examples of problem shifts. The pupils begin by trying to prove that V - E + F = 2 for all polyhedra (p. 6) but move on to examining questions such as whether "all Cauchy-polyhedra are Eulerian," (p. 65). Lakatos recognizes this as a general pattern: "Naive conjectures and naive concepts are superceded by improved conjectures (theorems) and concepts (proof-generated or theoretical concepts) growing out of the method of proofs and refutations. (p. 91).
Lakatos first makes extensive use of the phrase "progressive and degenerating problem shifts" in his critical essay, "Changes in the Problem of Inductive Logic" (1968). The provenance of this paper is relevant to both its tone and content. In 1965 an International Colloquium in Philosophy of Science was held at
Bedford College in London. Lakatos took a very active role in planning the conference and was senior editor of the published proceedings. Three volumes appeared in 1967-78 structured around problems in mathematics, inductive science, and philosophy of science. A fourth volume, Criticism and the Growth of Knowledge, appeared in 1970. Lakatos played an active role as editor, inviting participants in the debates to present reconstructed and expanded versions of their informal remarks. Lakatos also extended his own comments and the result was two monograph length essays.
Lakatos had recently joined Popper's department at the London School of Economics and the Conference was set up to foster a confrontation between Popper's philosophical views and those of two opposing traditions -- modern inductivists such as Carnap and Salmon on the one hand, and "irrational relativists" such as Kuhn on the other. The L.S.E. even had a secret weapon saved up for the inductivists, a new paradox which was presented by David Miller, then a graduate student at the L.S.E. The verbal skirmishes at the Conference were inconclusive, as philosophical debates usually are, although Carnap scored rhetorical points with his remark about the impossibility of defending inductive arguments to those who were "inductively blind" and his discovery that the distance function must be asymmetric since his views seemed to be farther from those of Sir Karl, than Sir Karl's were from his! On the other hand, David Miller's paradox certainly appeared to be devastating and Popper repeatedly referred to it.
However one may wish to score the debate at the Conference, Lakatos certainly "wins" the published volume. His essay begins with a description of the bustling problem-solving activity that goes on within a research programme (he is not yet using this as a technical term.), pointing out that one frequently ends up solving "very different problems from those one has set out to solve" (PIL, p. 316). He then lays out the two kinds of shifts: "One may solve a more interesting problem than the original one. In such cases we may talk about a `progressive problem-shift.' But one may solve some problems less interesting than the original one; indeed, in extreme cases, one may end up with solving (or trying to solve) no other problems but those [technical difficulties] which one has oneself created while trying to solve the original problem. In such cases we may talk about a `degenerating problem-shift.'" PIL, pp. 316-317.
What follows is the sorry tale of the degeneration of Carnap's inductive logic program -- the move from seeking the degree of confirmation of universal laws to mere instance confirmation, the retreat to continuum of inductive methods, the devasting discovery of language dependence, and the subsequent search for the "right" language for science, a search which may itself require inductive science.
Lakatos concludes: "With the abdication of the inductive judge even the last tenuous threads are severed between inductive logic and the problem of induction. A mere calculus of coherent beliefs can at best have marginal significance to the central problem of the philosophy of science. Thus, in the course of the evolution of the research programme of inductive logic its problem has become much less interesting than the original one: the historian of thought may have to record a `degenerating problem-shift.'" PIL, p. 373.
I happen to agree with Lakatos' assessment of Carnap's research programme -- it is not an area of research which I would recommend to new graduate students. However, I don't think Lakatos' analysis really provides a reason for this evaluation of the program. He says we have degeneration when an important problem is replaced by one of less interest. But what makes a problem interesting in the first place? And can not a proof that a utopian quest is impossible in itself constitute progress? Is it degeneration or an increase in sophistication when we give up a search for the philosopher's stone, a perpetual motion machine, a completeness proof for arithmetic, or a non-zero degree of confirmation for universal generalizations?
In another essay Lakatos himself provides an example of a problem shift, the evaluation of which he admits is controversial. He describes Popper's "all-important shift in the problem of normative philosophy of science," (I, p. 140): For Popper, methodology no longer refers to rules for making scientific discoveries; instead it consists of "directions for the appraisal of solutions already there" (I, p. 140). Then in a footnote Lakatos voices reservations: "I should like to say here that I always had doubts about whether this (no doubt progressive) problem shift had not gone a bit too far" (I, p. 140). He goes on to cite with approval Polya's interest in finding a heuristic which is both rational and non-psychologistic (I, p. 140). But then might not an extreme "friend of discovery" therefore declare Popper's original problem shift degenerating because it decisively moves away from the important problem of finding a genuine logic of discovery?
Lakatos, perhaps even more than Popper, has alerted us to how frequently we shift the central problems of our inquiry and he has urged us to critically appraise these shifts, but as yet we have no theory of how that appraisal might be carried out, especially in the field of philosophy. Let us now see what he says about progressive and degenerating problemshifts within the context of scientific research programmes.
The first published version of Lakatos' methodology of scientific research programmes (MSRP) appeared in the 1968 Proceedings of the Aristotelian Society. The longer and better known 1970 exposition forms the core of the fourth volume which came out of the Bedford Conference. That book begins with a debate between Kuhn and Popper. Lakatos' theory is offered as a third alternative which is intended to synthesize the descriptive superiority of Kuhn's theory of science (there are long periods of quasi-stability) with the normative bite of Popper's approach to philosophy of science.
According to Lakatos, most of mature science is done under the aegis of a research programme. A research programme consists of a hard core of metaphysical and theoretical postulates not to be given up, plus a positive heuristic, i.e., a rough plan for making increasingly sophisticated models of the phenomena to be explained. Thus, we can think of a research programme as generating a series of theories T1, T2, ... Tn each of which makes empirical predictions about the world. Although the research programme cannot be falsified in Popper's sense, it can be appraised.
Here is how Lakatos describes the appraisal: "Let us say that a series of theories is theoretically progressive (or `constitutes a theoretically progressive problemshift') if each new theory has some excess empirical content over its predecessor..." (I, p. 33). He then goes on to define an empirically progressive problemshift (the novel prediction is corroborated) (I, p. 34) and a degenerating problemshift, which includes cases where the new theory is ad hoc in the sense of not being generated by the positive heuristic.
The adequacy of this theory of appraisal need not concern us at the moment for it is immediately obvious that what is being directly evaluated are theories, not problems! Lakatos admits this in a footnote: "the appropriateness of the term `problemshift' for a series of theories rather than of problems may be questioned. I chose it partly because I have not found a more appropriate alternative -- `theoryshift' sounds dreadful -- partly because theories are problematical, they never solve all the problems they have set out to solve" (I, p. 34). He makes a similar justification of his terminology in Arist, p. 164.
5.7 Final Comments
But where does this leave us with respect to our inquiry into the nature and evaluation of problems? Maybe we could say something like the following: If T2 is theoretically progressive over T1, then testing T2 is a more important problem than testing T1. Or perhaps it would be more in the spirit of Lakatos to say that if one research programme is progressing at a slower rate than some rival, then the problem of generating a new theory within the rival is more important that continuing to work in the original programme. It would not be surprising if our account of problems turned out to be dependent on an account of theories. Lakatos has provided evocative terminology which strongly suggests that however we end up evaluating problems, it will make more sense to make the measure a comparative one instead of trying to set up absolute measures of worth.
Lakatos' definition of a Research Programme also provides valuable hints about how we might begin to articulate the constraints on acceptable problem solutions which we alluded to in our discussion of Kuhnian puzzles which arise within the context of a paradigm. The problem of explaining magnetism for Descartes was constrained by the hardcore postulates of the Mechanical Philosophy which denied the existence of forces other than those involved in the collisions of corpuscles. In the Newtonian programme, by contrast, action-at-a-distance was permissible but all forces had to be central forces, i.e., their strength had to vary smoothly with distance. Lakatos reminds us that these constraints can be expressed propositionally and subjected to rational discussion. We need not describe them in terms of tacit or unconscious assumptions which can only be changed through conversion experiences. (For an excellent discussion of the piece-meal dismantling and restructuring of cognitive systems, see Thagard's Conceptual Revolutions.)
5.8 Laudan and Problem Weights
All of the philosophers dealt with so far -- Popper, Kuhn, Lakatos -- think problems are an important part of scientific methodology, but Laudan is the first to base his epistemology on problems. In his 1977 Progress and Its Problems: Towards a Theory of Scientific Growth, Laudan inverts the traditional conceptual hierarchy by defining rationality in terms of progress and basing theory appraisal on problem appraisal instead of vice versa.
Here is a summary of Laudan's core theory of scientific growth (I am omitting his account of research traditions): The aim of science is to solve cognitive problems of which there are two basic types -- empirical and conceptual. Theories are appraised according to their problem-solving effectiveness, which in turn is a function of both the number and weight of the problems solved. (Theories get plus marks for solving empirical problems and minus points for generating empirical anomalies or conceptual problems.)
Progress is defined as an increase in problem-solving effectiveness. Scientific rationality consists in following procedures designed to maximize scientific progress. However, philosophical theories about what procedures can or should be used change. All we can do is rely on the best available current methodology. (I also omit Laudan's metatheory about how to appraise methodologies.)
To fully appreciate how completely Laudan's account relies on the concept of problems and solutions, contrast the above scheme with a more standard account: The aim of science is truth/knowledge/explanatory/power. Theories are appraised according to their empirical adequacy (and simplicity). Progress is defined in terms of an increasing degree of empirically adequate content (and conceptual coherence). Rational acceptance depends on empirical adequacy; rational pursuit depends on empirical promise. Has Laudan just switched terminology or does he have a radically new approach to science? Some of each, I believe, but let's look in detail. I will begin with his theory of empirical problems.
a. Empirical Problems
According to Laudan an empirical problem is "...anything about the natural world which strikes us as odd, or otherwise in need of explanation...Our theoretical presuppositions about the natural order tell us what to expect and what seems peculiar or `problematic' or questionable (in the literal sense of that term)." (p. l5) This general characterization reminds us of Popper's cases of "violated expectations" or refutations. However, Laudan's own examples of what he calls an "archetypal" sense of the concept are all cases where the explanandum is an empirical generalization:
"We observe that heavy bodies fall toward the earth with amazing regularity. To ask how and why they so fall is to pose such a problem. We observe that alcohol left standing in a glass soon disappears. To seek an explanation for that phenomenon is, again, to raise an empirical problem. We may observe that the offspring of plants and animals bear striking resemblances to their parents. To inquire into the mechanism of trait transmission is also to raise an empirical problem." (pp. 14-15)
At least two out of three of these examples do not fit his definition. The "regularity" of falling bodies is not easily observed. First of all, what turns out to be uniform is the constant change in velocity. Secondly, as Galileo noted, wooden and metal balls do not fall at exactly the same rates. For nearly two thousand years (Aristotle - Galileo), what required explanation was the variable rate at which different bodies fell. A similar remark could be made about the inheritance problem. What most preoccupied students of reproduction for a long time was the production of monsters, variations from the "form" or "ideal type." And astronomers were most puzzled by the irregular wanderings of the planets, not the smooth arcs of the sun, moon, and stars. However, I agree that both empirical regularities and oddities can trigger the search for explanations.
Laudan emphasizes that there is not a one-to-one correspondence between facts and empirical problems. First of all, "a problem need not accurately describe a real state of affairs to be a problem: all that is required is that it be thought to be an actual state of affairs by some agent." (p. 16) Laudan gives as an illustration, Oresme's report that hot goat's blood could split diamonds. (p. 16) Secondly, "To regard something as an empirical problem, we must feel that there is a premium on solving it... It was known since the earliest times, for instance, that most trees have green leaves. But that 'fact' only became an 'empirical problem' when someone decided it was sufficiently interesting and important to deserve explanation." (p. 17) Again, I would have preferred an example which involves an implicit refutation. "Why is the sky dark at night?" (Olbers paradox) only becomes a problem when people start integrating the background illumination to be expected from all distant stars and calculate that it should be enormous.
In any event, for Laudan empirical problems are putative facts which when viewed against the framework of our theoretical presuppositions strike us as being odd, interesting, or important enough to deserve explanation. Might we therefore conclude that to say that scientists search for solutions to empirical problems is just another way of describing the search for Hempelian explanations? Laudan emphatically denies this possibility.
First of all, as we have seen above, Laudan's explananda need not be true. (Hempel's are.) Secondly, Laudan allows that a theory which solves a problem may entail only an approximate statement of the empirical result. (In his later work Hempel does discuss this possibility.) Thirdly, Laudan insists that an explanatory theory need not be true. There is a very clear sense in which Ptolemy`s theory solved the problem of retrograde motion while failing to solve the problem of the change in apparent magnitudes of the planets. Hempel requires that explanations have true premises, but he also has a notion of law-like to describe statements which satisfy all the requirements for nomicity except truth and speaks of explanation proposals when dealing with generalizations which are only law-like.
However, Laudan would not find this weakened version acceptable for he goes on to say that "in determining if a theory solves a problem, it is irrelevant whether the theory is true or false, well or poorly confirmed" (pp. 22-23). Laudan is himself aware that his view is "heretical" (p. 24) amongst philosophers of science. Even Popper, no believer in confirmation, would require that proposed solutions to scientific problems be independently testable, and that we try to replace any proposed solution which is known to be false.
I think the best way to understand Laudan here is as follows. Since he believes that scientific standards have changed dramatically as science has evolved, he makes his trans-historical characterization of methodological concepts as weak as possible. So he says things like the following: "...any theory, T, can be regarded as having solved an empirical problem, if T functions (significantly) in any schema of inference whose conclusion is a statement of the problem." (p. 25) (Actually this is probably too strong because elsewhere he allows that only an approximation be entailed.) As it stands, this would allow deduction from totally absurd premises to count as problem solutions. However, Laudan emphasizes that each scientific epoch imposes additional requirements: "One of the richest and healthiest dimensions of science is the growth through time of the standards it demands for something to count as a solution to a problem." (p. 25) A simple example would be increasing standards of precision for experimental accuracy.
So for Laudan, whether or not a theory counts as a solution can only be answered relative to community standards: "In very rough form, we can say that an empirical problem is solved when, within a particular context of inquiry, scientists properly no longer regard it as an unanswered question, i.e., when they believe they understand why the situation propounded by the problem is the way it is. [my italics]" (p. 22) But he also hints that the community standards improve: "In the history of many disciplines, humanistic as well as scientific, one can perceive a gradual tightening and strengthening of the threshold at which a theory will be conceded to be a solution to the relevant problem." (p. 26)
It is easy to find examples of changing standards -- any history of statistical theory or experimental apparatus or scientific institutions is full of them. But is there also a basic core of scientific desiderata which remain invariant, although our optimism about how close we can come to achieving them may vary? In particular, if a particular discipline considers the truth or falsity, or degree of empirical adequacy of a theory irrevelant (Laudan's word), (and not just perhaps one factor among many), what do we mean to say if we nevertheless call it a scientific discipline? And given Laudan's objective of comprehending broad areas of the history of ideas (cf. pp. 189-192) one wonders why he insists on the logical entailment condition for problem solutions (assuming this is intended to be a necessary condition) because many non-scientific explanations work through structural analogies or metaphors, not deduction. But let us pursue the rest of his analysis of problems and not get side-tracked on to these intriguing epistemological and historical questions!
Solved empirical problems count for a theory, according to Laudan; anomalies count against it, unsolved problems "simply indicate lines for future theoretical inquiry." (p. 18) Since his main interest is in evaluating theories through the problems they create or solve, it is not surprising that he does not dwell on unsolved problems, except to make the interesting point that it often happens that it is unclear to which domain of science a phenomenon belongs (cf. Brownian motion) and when that is the case we can hardly blame a theory for not explaining the effect in question. Laudan's exact evaluation of the weight of unsolved problems is a little murky. At one place he says the issue is a complex one, "but a good first approximation... is this: unsolved problems generally count as genuine problems only when they are no longer unsolved." (p. 18) Later he is more emphatic: "Hence, in appraising the relative merits of theories, the class of unsolved problems is altogether irrelevant." (pp. 21-22).
Perhaps it is Laudan's extreme concern about assigning phenomena to fields which motivates his definition of anomalous problem as "an empirical problem which a particular theory has not solved but which [a competitor has]." (p. 17) "Whenever an empirical problem, p has been solved by any theory, then p thereafter constitutes an anomaly for every theory in the relevant domain which does not also solve p." (p. 29) "The only reliable guide to the problems relevant to a particular theory is an examination of the problems which predecessor -- and competing -- theories in that domain (including the theory itself) has already solved." (p. 21)
Laudan is aware that his definition of anomalous problem would not include as instances most Popperian refutations or Kuhnian recalcitrant anomalies: "In stressing that a problem can only count as anomalous for one theory if it is solved by another the analysis seems to run against the common view that one sort of anomaly, the refuting instance, poses a direct cognitive threat to a theory, even if it is unsolved by any competitor. If a theory predicts a certain experimental outcome (say O) and experiment reveals that ~O is the case, then surely, ~O constitutes an anomaly for the theory even if no other theory can solve ~O? As paradoxical as it may seem, this is generally unsound....unsolved refuting instances are often of little cognitive significance." (p. 30)
Except for what we might call the case of field ambiguity (e.g., who should explain the apparent enlargement of the moon when it is near the horizon, psychologists or astronomers?), Laudan gives no reason for his discounting of refutations which no other theory has solved. Of course, as we pointed out in our discussion of Popper, there is often a tough Duhemian decision to make about which hypothesis to blame for a refutation, and I would agree that until that is cleared up, the theory is not given a large black mark. But solving the Duhemian problem is often independent of finding an alternative to the main theory. Thus Mendeleev said the discovery of the rare-earths "broke" his Periodic Table -- and this was admitted long before the atomic number theory was proposed.
And Laudan himself reverts to the standard view in this example: "It was Prout's view that all the elements were composed of hydrogen and, consequently, the atomic weights of all elements should be integral multiples of the weight of hydrogen. Shortly after the appearance of this doctrine in 1815, numerous chemists pointed to seeming exceptions or anomalies. Berzelius and others found that several elements had atomic weights incompatible with Prout's theory (e.g., weights of 103.5 for lead, 35.45 for chlorine, and 68.7 for barium). These results constituted very serious anomalies for Proutian chemists." (p. 31). Note that by Laudan's strict definition, fractional atomic weights did not constitute anomalous problems for Prout's theory since no other theory had as yet explained them.
In addition to his basic trichotomy of solved, unsolved, and anomalous problems which respectively carry positive, zero, and negative weights, Laudan introduces some other factors which influence the weighing of problems such as the generality of the problem (p. 35); the degree of discrepancy between theory and experiment (p. 39) and the age and recalcitrance of an anomaly. (p. 39) Particularly interesting is his notion of "problem inflation by archetype construction. At a more subtle level, there are other ways in which theories may endow certain empirical problems with greater significance than others. As we shall see later in detail, many theories single out, from the range of problems in the domain, certain empirical situations as archetypal." (p. 34) As examples he cites the Leyden jar for Franklin and the laws of impact for Descartes. One is reminded here of Bacon's concept of Prerogative Instances and Kuhnian exemplars.
b. Conceptual Problems
Let us now turn to Laudan's second category, what he calls conceptual problems. Laudan makes the dubious claim that not just philosophers but also historians of science have "largely ignored" the crucial role of this nonempirical type of problem. (cf. pp. 45-47 and 66) I will snipe away at Laudan's sociological thesis about neglect as we go along. Our main concern is to present his own theory of conceptual problems.
First he discusses conceptual problems which are internal to the theory, such as conceptual ambiguity, circularity, or self-contradiction. Contrary to Laudan, in my opinion both historians and philosophers of science have been exceedingly interested in this kind of problem. The whole point of axiomatization by the logical positivists was to clarify the status of claims about the one-way speed of light or survival of the fittest. Historians have described in detail the gradual clarification of concepts such as gravitas, vis viva, element, and cell and controversies over the "intelligibility" of notions such as action-at-a-distance, infinitesimals, and quantum jumps. Laudan does not dwell long on this category of problem, possibly because he thinks they have in general played a less decisive role in the history of science than have the problems which arise when a theory is in conflict with a doctrine outside itself.
Laudan classifies what he calls "external" conceptual problems along two dimensions, one logical and one substantive. Let us illustrate the latter dimension first by applying Laudan's terminology to a familiar example. In Galileo's time, Copernican theory faced difficulties on a variety of fronts. It was inconsistent with the best physical theory available at the time -- Aristotle's mechanics; Laudan calls this an "intra-scientific" problem, p. 55, (see also NK). By relying on telescopic data, it violated Aristotle's common-sense methodological norms for reliable observation (the telescope distorted the senses, added colored fringes to images, and inverted the apparent sizes of stars and planets); Laudan calls these "normative difficulties" and claims that conflicts over methodology have been "the single major source for most of the controversies in the history of science" (p. 58). Thirdly, Galileo's claim that the earth moves was inconsistent with contemporary religion; this is an example of what Laudan calls "worldview difficulties," a category which would also include conflicts between science and metaphysics, such as Einstein's concern with the non-deterministic, non-causal character of quantum mechanics.
Again I am surprised that Laudan thinks that these sort of problems have been downplayed by historians and philosophers of science, especially since Laudan admits that "how serious the problem is for the theory depends on how well entrenched the nonscientific belief is and upon what problem-solving capabilities we would lose by abandoning it." (p. 64) Perhaps the disagreement between Laudan and other post-positivist philosophers of science is not about the possible relevance of metaphysics or methodology, but about how tough our standards for appraising their "problem-solving capabilities" should be.
Let us now turn to the different logical relationships which may enter into external conceptual problems. (p. 54) Laudan correctly points out that inconsistency is not the only sort of inter-theoretic relationship which can create problems. Sometimes we may have two compatible theories which are disjoint although we would expect there to be a unified account of their two domains -- thus the search for a unified field theory. Other times we may expect a theory in one domain (e.g., thermodynamics or cognitive psychology) to be reducible to a theory at a more fundamental level. Until that occurs we are somewhat dissatisfied with both sides of the picture. As these few examples indicate modern historians and philosophers of science are keenly aware of the problems of theory unification, reduction, and replacement.
Laudan's theory of the weighing of conceptual problems can be easily summarized. First of all, conceptual problems always count against a theory and he believes "most conceptual problems are of greater moment than most empirical anomalies." (p. 64) (The last generalization appears to be based on his reading of history, not on normative considerations.) He also introduces a rule of thumb for each dimension of his classification of external problems: Inconsistencies are more serious than weaker forms of "tension." (p. 65) And inter-theoretic conflict is more acute the more confident we are in the problem-solving ability of the incompatible theory. (p. 65)
As we have already seen, Laudan considers internal conceptual problems to be less important than external ones. Among the internal problems, self-contradiction is the most acute. Laudan makes the strong claim that unless one "can somehow `localize' the inconsistency, the only conceivable response to a conceptual problem of this kind is to refuse to accept the offending theory until the inconsistency is removed." (p. 49) (In a footnote he distinguishes acceptance from pursuit.) His last guide-line for weighing refers to the "age" of the problem, the rationale being that if the problem is a newly discovered one we may hope that a minor modification will set things right. (p. 51)
5.9 Final Comments
This concludes my summary of Laudan's theory of the relative weights of problems. You will recall that his primary goal was to use problems to evaluate the cognitive status of theories. For that purpose I find his account quite unsatisfactory (see NK and Hattiangadi for details). To mention just one objection, his criteria for a problem solution are much too weak. However, that and other epistemological difficulties need not vitiate his account as a theory of the evaluation of problems simpliciter. And for this latter task I think he has made an excellent beginning by giving a more systematic presentation of the types of problems discussed by Popper, Kuhn, Lakatos, et. al.
Nevertheless, there are gaps and flaws in his account. In addition to the criticisms already made above. I will mention the following: Laudan thinks that his distinction between empirical and conceptual problems reflects an object-level, meta-level distinction with only empirical problems being substantive questions about the world. (p. 48) Only a non-realist would be tempted to say such a thing. As the Galileo case reminds us, all of the "external conceptual" problems with Copernicism directly concerned its truth. There are meta-objections we may raise about a theory--for some people, the demand for simplicity may be independent of questions about substance. But as this example illustrates, it will probably be impossible to make a theory of problems which is invariant with epistemology although we can certainly try to keep the dependency to a minimum.
There are also some formal flaws with Laudan's account. Suppose T1 (our theory) is inconsistent with T2 (a theory we are not much interested in). How serious a problem for T1 is this conflict? Well, it depends on the status of T2, but that in turn depends on how serious for T2 its conflict with T1 is which in turn depends on weighted sum of the problems solved and generated by T1 -- So we are unable to get started on our original weighing task.
We must credit Laudan with bringing the philosophical problem of classifying and weighing scientific problems onto center stage, but we must not forget that Laudan's purpose in introducing problems as an important element in philosophy of science is in order to evaluate theories and research traditions. Thus he is trying to replace the classical accounts of theory appraisal in terms of degree of confirmation, corroboration or explanatory power with a story about weighing the successes and failures of theories as problem solvers.
Our purpose in focusing on problems is rather different. We are more interested in the initial phases of the continuing cycles of scientific inquiry -- in the choice of research projects, in the structure of the questions which lead to new theoretical developments. Thus our typology of scientific problems and our rankings of their importance would not be expected to coincide with Laudan's even if we shared similar general philosophical views which we obviously do not! On my account if a theory generates lots of brand new unanswered questions, (e.g., Dalton's atomic theory raises the problem of the relative weights of atoms), that obviously need not count against the theory. If anything, we land its fertility.
Neither would I conclude that such unsolved problems are not important or of low weight (as does Laudan) unless there is a competing theory which does solve them! I can think of no better way to induce scientific stagnation.
The moral of the story is simple: The role of unsolved problems depends crucially on whether we're talking about the epistemological credentials of a theory or the evaluation of a research project.
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