The 1950s and 1960s saw a dramatic change in geology, namely the acceptance of the continental drift hypothesis as a part of the plate tectonics theory. One interesting thing about this change is that some of the participants in the change described it as a 'revolution' citing Kuhn (1962) explicitly. On the other hand, the interpretations by historians, philosophers, and sociologists of science are fairly diverse. The purpose of this paper is to review the different interpretations and critically analyze their plausibility. Section 2 summarizes the standard description of the acceptance of the continental drift hypothesis. Sections 3 through 7 deal with different interpretations of the story. Section 3 deals with the Kuhnian interpretations of the change by Wilson and other geologists. In Section 4 we see some criticisms of the idea of revolution. Section 5 summarizes interpretations from Lakatos' or Laudan's point of view. Section 6 deals with perspectives from evidential support and confirmation theory. Section 7 deals with social perspectives. In Section 8, I sum up the debate critically.
2. The history of the plate tectonics revolution
In this section, I outline the standard account of the history of the acceptance of continental drift as a part of plate tectonics theory (in a somewhat Whiggish way). The descriptions mainly depend on Marvin (1973) and Hallam (1973, 1983) supplemented by other authors in some points.
There were several precursors who had noticed the similarity of the coastlines of Africa and South America in the 19th century and early 20th century, but Alfred Wegener was the first person who made a serious and influential attempt to explain this fact and other facts by lateral movements of continents. He publicized this idea first in his lectures and short papers in 1912, and in 1915 he summed up his argument in a book, Die Einstehung der Kontinente und Ozeane (Wegener  1966).
Basically Wegener used three sorts of evidence: geological, paleontological (biological), and paleoclimatic. Among geological evidence, the most striking one is the similarity of the coastlines of both sides of the Atlantic, but this similarity becomes even more striking by comparing the rocks on both continents. It was already known that there were very similar sequences of sediments called Gondwana Series in several different continents like South America, Africa, India, Australia, and Antarctica. Wegener showed how similar this series of sediments in South Africa and that in Brazil were. If these continents were not connected during the geologic period (this series ranges from the Carboniferous to the Jurassic), this is unexplainable. Another sort of evidence was the fossil records in Africa and South America. In the Paleozoic the records indicated that many plants and animals were common to these continents, but after the Cretaceous the similarity decreased enormously. Wegener also used the distribution of living animals like earthworms in these continents as evidence. These biological facts indicate that the two continents were once connected. The third sort of evidence was the world climate in the Permo-Carboniferous period. The moraine deposit showed that South Africa, Argentina, southern Brazil, India and Australia were capped by an ice-sheet in this period. If these continents had been in their present positions during that period, this indicated that a considerable part of the southern hemisphere was covered with an ice-sheet. But the evidence from the northern hemisphere of this period showed a tropical climate. This is absurd.
Some of the evidence can be explained if we assume earlier land bridges between continents, but Wegener denied this possibility because of the structural difference between continents and ocean basins. Instead, he proposed the hypothesis that continents can move laterally. According to him, there was a supercontinent 'Pangea' in the Upper Carboniferous period. Africa and South America started to divide in the Cretaceous period; India was separated from Africa in the Jurassic and moved northward (the Himalayas are a result of the compression caused by this movement); North America and Europe were finally divided in the Quaternary; and so on.
Even though Wegener's continental drift hypothesis was taken seriously, and even found several supporters, the general reaction from the geological community was negative. At that time there were several other accounts that explained some of the evidence Wegener used. One is the aforementioned land bridge theory, and this is connected to the contraction theory proposed by Suess in the 19th century. According to this theory, the earth has been contracting because it has been cooling down. The followers of this and other similar theories (they are often called 'fixists') attacked Wegener's hypothesis in several respects, but the most serious attack was on the problem of mechanism. Wegener thought that the continents somehow plough through the ocean floor, and proposed two possible causes for this, i.e. the pole fleeing force and the tidal force. But these forces were criticized as being too weak for such great movements. Some of the followers of the drift theory proposed alternative mechanisms to overcome this problem, such as Holmes' theory that the convection currents inside the earth drives the continents, but they could not convince opponents. Some historians pointed out another major reason why the drift theory was rejected; Wegener was not a geologist in his training, but a meteorologist (Hallam 1973, 113; Cohen 1985, 454; Allègre 1988, 19).
In the 1940s there were few followers of the drift theory. But in the 1950s the situation started to change in two fields: paleomagnetism and oceanography. The phenomenon that the lava is weakly magnetized in the direction of the magnetic field at the time it cools has already been known for a long time, but in the 1950s a highly sensitive magnetometer was constructed and a wider range of rock samples became available. The research showed that the magnetism of rocks preserves the direction of the field of the time they were made. This new evidence was used to determine the place of the north pole in geological ages, and revealed surprising facts. First, P.M.S. Blackett's group in London announced that the land mass of England had rotated clockwise 30 degrees and drifted northward (assuming the place of the north pole had remained the same). They also studied rocks from India and concluded that India has drifted northward 7000 kilometers within the last 80 million years. S.K. Runcorn's group in Newcastle tried to explain the phenomena by assuming that the north pole, not the continents, had moved over the millions of years (this idea is called 'polar wandering'). To prove this hypothesis, Runcorn's group investigated North American rocks. They proved the existence of polar wandering indeed, but at the same time they found a consistent difference between the trajectory of the north pole constructed from European rocks and that constructed from North American rocks. This consistent difference disappears by assuming that North America and Europe once made a continent as Wegener suggested. As a result, Runcorn converted to the drift theory. This surprising result, however, did not lead to a wide acceptance of the drift theory. Marvin points out that the majority of geologists were unfamiliar with paleomagnetism, so they could not appreciate the result (Marvin 1973, 148). LeGrand suggests that the existence of opposing camps in paleomagnetism let people adopt a 'wait-and-see' attitude (LeGrand 1988, 155).
Another change came from oceanography. The introduction of echo-sounding equipment enabled a thorough survey of the ocean floor, and revealed interesting structures. Mid-oceanic ridges like the mid-Atlantic ridge were found to be a global system, 60,000 kilometers in length. These mid-oceanic ridges are also characterized by their seismicity and heat flow. Fracture zones, fault-like structures cut across the oceanic ridges, were also found. Another surprising finding was that there were no sediments in the ocean older than mid-Cretaceous. To account for these new findings, H. Hess proposed the sea-floor spreading hypothesis in 1960 (published in 1962). According to this hypothesis, the sea floor was created at mid-oceanic ridges by the convection of the earth's mantle, and spread from there. This hypothesis has an immediate implication for the continental drift theory. Continents are passively carried by this movement, so they do not have to plough through the ocean basin.
People noticed that the sea-floor spreading hypothesis leads to some testable predictions. The first is the so called Vine-Matthews-Morley hypothesis. By the development of paleomagnetism, it was known at the time that the magnetic field of the earth reverses periodically (the so called 'magnetic reversal' phenomenon). On the other hand, it was also known that the magnetization of ocean-floor rocks shows curious patterns, namely normally magnetized rocks and reversely magnetized rocks are found in side-by-side strips. F. Vine noticed during his research on the Indian Ocean that if the sea-floor spreading hypothesis is correct, these strips record the magnetic reversals at the time the rocks were created. He published this idea with his supervisor Matthews in 1963. (Actually L. W. Morley came up with the same idea independently at about the same time, but his letters to Nature and Journal of Geophysical Research were both rejected; see Glen 1982, 297-302.) Another prediction is the existence of the 'transform fault.' In 1965, J. T. Wilson showed that if the sea-floor spreading hypothesis is correct, the fracture zones between ridges should show a specific kind of movement, and Wilson named this the 'transform fault.'
A remarkable confirmation of the Vine-Matthews-Morley hypothesis was made by W.C. Pitman at the Lamont Observatory. The Vine-Matthews-Morley hypothesis implies that the stripes should be symmetrical on either side of the ridges. Pitman analyzed several profiles of sea-floor magnetization across the Pacific-Antarctic Ridge, and found that one of the profiles, the Eltanin 19 profile, showed remarkable symmetry, exactly as implied by the hypothesis. This profile was presented at the April meeting of the American Geophysical Union in 1966. The presentation on the Eltanin 19 profile "had indeed overwhelmed the audience at the A.G.U. meeting; seafloor spreading was suddenly ascendant. A sense of of the import of that moment pervaded the audience" (Glen 1982, 347). Wilson's 'transform fault' hypothesis was confirmed by L. Sykes. This confirmation by Sykes, presented in November 1966, "suddenly made it very difficult for anyone not to take the idea of transformation faults seriously" (Cox 1973, 290). And, since the idea of transform faults is a logical consequence of the sea-floor spreading, this also meant the acceptance of the theory. The consensus for the plate tectonics theory was formed rapidly; "[f]or American scientists, the change took effect in the winter of 1966. Until then most of them had retained confidence in continental stability; but by the spring of 1967 a reaction was in full swing." (Marvin 1973, 2) Some people describe the sudden change as the "bandwagon effect" (Marvin 1973, 189; LeGrand 1988, 256-259). In 1967, McKenzie and Parker introduced the notion of 'plate' and explained its geometrical characteristics. The whole surface of the earth is covered with several huge plates (most of them including both continental and oceanic crusts) and other small plates. After 1966/1967, this plate tectonics theory has remained orthodox geology, even though there are still a few geologists who pursue other models (Marvin 1973, 182-189; Stewart 1990, 116-121).
Thus told, the success story of the continental drift theory seems to be clear and unproblematic. But once we start to reflect upon the details of the story and their philosophical implications, the picture suddenly becomes uncertain. Above all, why did the plate tectonics theory succeed where Wegener, Holmes, and paleomagnetism had failed? What are the decision processes of the scientists? Many geologists, historians, philosophers, and sociologists have tackled these questions in various ways. The following sections deal with these attempts.
3. Kuhnian interpretations of this history
Some of the geologists taking part in the revolution were well aware of the revolutionary character of what they were doing, and expressed their reflections in Kuhn's (1962/1970) terminology. In this section, we look at four of them, Wilson, Cox, Marvin, and Hallam.
Among them, J. Tuzo Wilson was the first who explicitly mentioned Kuhn's notion of 'scientific revolution.' As early as 1963, he declared that "earth science is ripe for a major scientific revolution" (Wilson 1963, quoted in Takeuchi et al. 1967, 244). Wilson did not mention Kuhn's work at this point, but later he admitted that he had gotten the idea of revolution from Kuhn (Cohen 1985, 565). In his (1968), Wilson referred to Kuhn explicitly (317). Wilson emphasized Kuhn's idea that "the essence of the revolution was not any improvement in techniques, not more or better data, not an advance in mathematics; it was a change in ideas" (Wilson 1968, 317). Wilson added a normative reading to it by saying "all the great scientific revolutions" had this character (ibid.). He even said that "[e]arth science has not progressed as it should" because of the wholly erroneous concept of the earth (ibid.).
Cox (1973) also affirms the Kuhnian interpretation of the plate tectonics revolution, with different emphases. Cox characterizes a Kuhnian revolution by discontinuity between paradigms and by "a sudden acceptance by a sizable segment of the scientific community because of the presentation of new experimental data and compelling theoretical arguments in favor of the theories" (Cox 1973, 4-5). In this understanding, "the development of plate tectonics ... fits the pattern of Kuhn's scientific revolutions surprisingly well" (5). Cox provides a nice example supporting his case, i.e. Tanya Atwater's experience (Cox 1973, 535). She wrote to Cox: "It is a wonderful thing to have the random facts in one's head suddenly fall into the slots of an orderly framework. It is like an explosion inside. That is what happened to me that night [the night McKenzie and Parker explained to her the geometry of the plate concept] and that is what I often felt happen to me and to others as I was working out (and talking out) the geometry of the western U.S."
Marvin's (1973) account of the revolution is similar to Cox's. She describes the revolution as "[t]he story of continental drift as a geologic concept, with its slow, tentative beginnings and violent controversy, followed by the spectacular bandwagon effect which has swept up the majority of earth scientists," and claims that this story bears out Kuhn's thesis on scientific revolutions (Marvin 1973, 189). An interesting aspect of her use of the Kuhnian interpretation is that she uses this argument as a concluding part of the section dealing with remaining opponents to the plate tectonics theory after 1970. She suggests that the revolution was attained by ignoring to some extent difficult cases for the plate tectonics theory raised by the opponents, and that the true test of the theory will come when geologists turn to these difficulties (190).
Hallam (1973) gives the most detailed analysis from the Kuhnian point of view among the authors discussed here. He maintains that "[t]he earth sciences do indeed appear to have undergone a revolution in the Kuhnian sense and we should not be misled by the fact that, viewed in detail, the picture may appear somewhat blurred at the edges" (Hallam 1973, 107, 108). According to Hallam, the conflicting paradigms in this revolution are 'stabilist' and 'mobilist' paradigms (108). The 'stabilists' believe that the continents have remained fixed in position with respect to each other. Wegener started the revolution by attacking this paradigm from the mobilist's point of view, though some fifty years had passed before the full formation of the new paradigm (ibid.). Hallam analyzes the reason Wegener's hypothesis was not accepted from this perspective. He enumerates several factors like lack of evidence and inadequacy of mechanism, but he suggests that the "stabilist paradigm or Gestalt of the Earth" itself might be the crucial stumbling-block (109, italics in original). Hallam's analysis also emphasizes social factors in the revolution. For example, Wegener was not an accredited member of the professional geologists' club (113). Finally, sheer conservative prejudice played an important role. As a evidence of this, Hallam quotes R.T. Chamberlin's famous comment in the 1928 A.A.P.G. symposium: "If we are to believe Wegener's hypothesis we must forget everything which has been learned in the last 70 years and start all over again" (Hallam 1973, 113).
We shall see criticisms of these interpretations below, but some analyses are in order here. First, these geologists understand Kuhn differently one from the other. In general, Wilson's and Cox's understandings are rationalistic, while Marvin and Hallam see irrational sides. Between Wilson and Cox, Wilson emphasizes the normative aspects, while Cox is more descriptive. Between Hallam and Marvin, Marvin suggests the irrational side of the rise of the new paradigm using the expression 'bandwagon effect,' while Hallam concentrates on the irrationality of sticking to the old 'stabilist' paradigm. Therefore we should be careful when we criticize their interpretations. Secondly, when these geologists use Kuhn's name and the notion of 'scientific revolution,' they are not fully committed to Kuhn's view (even though their comments sound as though they are). Rather, they pick up several basic notions like 'paradigm' and interpret them in a way suitable for their understandings. For example, Wilson's emphasis on the progressive nature of the revolution and Cox's emphasis on "new experimental data and compelling theoretical arguments" (see above) are not incompatible with Kuhn, but they are far more rationalistic than Kuhn (in his (1962), at least). Marvin and Hallam look at more irrational sides of the paradigm shift, but still they drop many important parts of Kuhn's account, such as normal science as a problem-solving activity, anomaly, crisis, and so on. Above all, they seem to take the superiority of the new paradigm for granted (except for Marvin's somewhat sympathetic treatments of opponents of the plate tectonics theory), and as a result none of them mention the notion of 'incommensurability.' So we should carefully distinguish the Kuhnian interpretations of the geologists and Kuhn's own account applied to the plate tectonics revolution.
4. Criticisms of the Kuhnian interpretations
The above Kuhnian interpretations are criticized by several authors, and in this section we shall look at three of the critics, namely Ruse, Kitts, and Wood (other important critics, like Frankel, are discussed in other sections).
First, Ruse (1981) criticizes the Kuhnian interpretations by checking several aspects of Kuhn's own thesis. He sums up Kuhn's (1962/1970) four basic theses about scientific change as follows (245-246): first, the change has sociological aspects, for example the revolution is done by rather young scientists, and often old scientists remain hostile to the new paradigm; second, there is a psychological level in the revolution, something like a Gestalt switch or conversion experience; third, there is an epistemological dimension, namely the paradigm change involves the change in methodology and data; in this sense when we change the paradigm we see the world differently; finally, there is an ontological dimension, namely, when we change the paradigm, we are not only looking at the world differently but the world itself changes. Ruse examine these four aspects in turn. As for the sociological factors, Ruse points out that two of the advocates of the revolution, Hess and Wilson, were fairly old. But overall the sociological aspects of the revolution are consistent with Kuhn's descriptions. As for psychological aspects, Ruse quotes Atwater's conversion experience from Cox (1973; see above). This also squares with Kuhn's view. But other aspects of the revolution are hard to fit into the scheme. As for the change in methodology, Ruse finds a general methodology unchanged before and after the revolution. The methodology is Whewell's 'consilience of inductions,' that is, "the best kind of science explains in many different areas from one hypothesis" (Ruse 1981, 249). Both pre-plate-tectonics geologists and plate-tectonics geologists use this methodology. At a more specific level, Ruse looks at Lyell's three guidelines: actualism, uniformitarianism, and a steady-state view of the earth. In plate tectonics, everything just keeps turning over and over endlessly, so this is a kind of steady-state. As for actualism and uniformitarianism, the mechanism of plate tectonics obeys these rules. Finally as for the ontological aspects, Ruse admits the theory-laden nature of scientific facts, but he thinks that geologists share much of their ontology before and after the revolution (like earthquakes, volcanos, etc.). So Ruse is not satisfied with Kuhn's view, but he thinks that Kuhn's is better than other metatheories (e.g. an evolutionary view of scientific change).
Second, let us look at Kitts' (1974, 1981) criticism. Kitts' main thesis (1974) is the continuity of the methodology of geology before and after the alleged revolution. To make this point, Kitts distinguishes theoretical paradigms and historical paradigms. A theoretical paradigm of geology comes from outside geology, namely from physics (Kitts calls this a 'superparadigm'; 118): "geologists never fault physical theory because it is incompatible with the record of physical events" (119). Therefore this is "a change going on inside geology which leaves the theoretical paradigm untouched" (ibid.). On the other hand, paradigms in geology like continental drift are historical paradigms, namely paradigms dealing with specific historical phenomena (123). Changes of such historical paradigms cannot change the whole discipline. Now the acceptance of the notion of 'plate tectonics' involves change of the methodology of the discipline, because the notion partly comes from physics. This change in 'superparadigm' enabled the revolution (124). But this does not mean that the change was discontinuous. Rather, this is the last step in the evolutionary change of geology from a cyclic view of earth history to a unidirectional, irreversible view (126-127). In his (1981), Kitts points out another continuous aspect of the methodology of geology. Geology is supposed not to have an organizing principle. But, on the other hand, the attitudes of geologists show that they are very confident about some kinds of factual claims, and this suggests that they have some reliable methodology. Kitts solves the paradox by distinguishing predictive and retrodictive uncertainties (224). When people say that geology has no organizing principle, they mean predictive uncertainty, namely the inability of geology to predict future events. But this is not the business of geology. Geology is a retrodictive science, namely a science for reconstructing past events. In this respect geology has a highly developed methodology. When geologists express uncertainty, they are talking about retrodictive uncertainty, i.e. uncertainty about the past events. This occurs when different sequences of events could lead to the same result. The development of geology is to eliminate such retrodictive uncertainties.
Wood's (1985) criticism is also worth mentioning. He casts a doubt on the premise that continental drift and the plate tectonics theory are one and the same paradigm. According to him, continental drift was "a pseudo-scientific hypothesis; kept afloat only by the hot air of discussion," because "there were no measurement to be made" and the supporters used "analogies, impressions, and argument" (Wood 1985, 193). On the other hand, plate tectonics is a 'hard' scientific theory (194). Wood even denies the status of the drift theory as an ancestor of the plate tectonics theory. He enumerates three ancestors of the plate tectonics theory: geometry on the surface of sphere, seismology, and 19th century fluidist (195-200). The behavior of plates cannot be understood without using the geometry of a sphere. The plates were defined solely by the observation of the global pattern of earthquakes. The 19th century supporters of a molten earth (who called themselves 'fluidists') often held closer views to the modern view than drifters. None of these things are related to the drift tradition, except that Holmes tried to connect the fluidist tradition with the drift theory by introducing convection current as a mechanism of the drift. Therefore, it is no wonder that the drift theory failed to persuade the geologists while plate tectonics succeeded; they are totally different. But this does not mean that Wood is an anti-Kuhnian. Wood distinguishes two paradigms, namely old Geology (with capital G) and newly created but long prepared Earth Sciences (with capital E and S) (193). One of the major differences between the two paradigms is that Earth Sciences deal with the Earth as a whole while Geology does not. Wood also contrasts "the fundamental subjectivity of geology" with "a scientific approach" of Earth Sciences (194). Needless to say, the drift theory and its rivals belong to the Geology paradigm, and the plate tectonics theory belongs to the Earth Sciences paradigm. In Earth Sciences, "the expert whose knowledge consists of the ability to name a plethora of fossils minerals, and identify the stratal age" is denigrated (223). Geology is "in danger of losing its soul" (ibid.). Here Wood is apparently talking about the "redefinition" of science and its proper problems by the new paradigm (see Kuhn 1962/1970, 103). In this sense he is much more truthful to Kuhn's account than the Kuhnian interpretations discussed above.
When we compare these three critics, there are several interesting similarities and differences among them. First of all, they all accept some aspects of Kuhn's theory. Kitts and Wood share a lot of insights into the nature of the plate tectonics revolution: for example, there is some qualitative difference between the continental drift theory and the plate tectonics theory; the plate tectonics revolution involves in a methodological change (in these respects, McKenzie and Oreskes, discussed below, also share the insights). But the conclusions they reach are remarkably different. Kitts finds a continuity in the evolution of the methodology, while Wood recognizes a discontinuity between Geology and Earth Sciences and even declares that Geology is about to die. On the other hand, both Ruse and Kitts emphasize the continuity in geology, but Ruse does not accept the evolutionary view Kitts subscribes.
It might be helpful to look at criticisms of Ruse and Kitts. Frankel (1981) criticizes Ruse because Frankel believes that epistemological and ontological discontinuities do exist in this revolution (208-209). Fixists opposed to the drift theory evaluate the evidence very differently from mobilists; for example, they totally dismissed the coast line similarities as accidental. As for ontological aspects, Frankel argues that by the transform fault hypothesis, the ontological status of the earthquakes has changed (though Frankel does not fully spell out how it has changed). Frankel himself has different reasons to object to the Kuhnian interpretations, as we will see in the next section. Kitts is criticized by R. Laudan (1981). The first point of the criticism is that Kitts takes Kuhn too rigidly. Kuhn himself is willing to allow a Darwinian revolution without any change in fundamental physical and chemical principles (229). (This point is a good reply to Ruse also.) Other points are related to the nature of geology. First, there was a geologist, T. Chamberlin, who criticized a whole cosmology to rescue his geology. Second, the mechanism problem of Wegener's theory was not so decisive as Kitts claims. So the relation between geology and physics is not as rigid as Kitts has indicated.
It seems to me that all of the authors discussed in this section and the last section agree upon the psychological (and sociological, largely) aspects of Kuhn's thesis. The most controversial part of the thesis is the methodological aspects. But I think that the Kuhnian interpretations by Wilson and others do not imply the methodological discontinuity, so they might agree with Kitts and Ruse. In this point Wood presents the most strong case for discontinuity, but there are several difficulties with his argument. To establish his case that the continental drift theory and the plate tectonics theory are in totally different paradigms, he should show that the founders of the plate tectonics theory, i.e. Hess, Wilson, Vine, etc. did not use the drift theory as their conceptual scheme. Abundant literature shows that this is not the case (see, for example, Frankel 1980, R. Laudan 1980, Glen 1982, 277). His claim about the death of Geology is also dubious. It seems to me Geology is alive and well as a subcategory of the earth sciences. Frankel's points against Ruse are not enough to establish the methodological discontinuity either. What he shows from his cases on earthquakes and coastline similarities is the theory-ladenness of observation, and this is a totally different matter from methodological discontinuity. So my tentative conclusion on this point is that I cannot find any reason to accept the radical discontinuity in the methodology of geology.
5. Research programmes and research traditions
Lakatos' (1970) 'research programme' approach and L. Laudan's (1977) 'research tradition' approach are both proposed to amend Kuhn's account of revolution from more rationalistic points of view. H. Frankel uses these approaches extensively in his works on the plate tectonics revolution. R. Laudan also uses these schemes. Their works have many aspects in common, so I deal with them together in this section.
Frankel's works (1979a, 1979b, 1980, 1981, 1987) mix up Lakatos' and L. Laudan's approaches in an interesting way. Frankel's objection to the Kuhnian interpretations explains why he uses these theories (Frankel 1981). According to Kuhn, a major scientific change takes one of two forms. One is the emergence of a new paradigm when there is no paradigm before that. The other is the replacement of a paradigm with another paradigm. But when we look at the plate tectonics revolution, we find several paradigms competing with each other. In analyzing this kind of competition, Lakatos and L. Laudan do much better jobs than Kuhn.
Frankel (1979a) analyzes Lakatos' approach and proposes two alterations of the account. Let us first look at Lakatos' view following Frankel's summary (22-28). A research programme is a sequence of theories which share some fundamental assumptions. These fundamental assumptions are called 'hard core,' and a theory consists of a hard core and a 'protective belt,' i.e. auxiliary hypotheses. When an experimental report or an observation contradicts the prediction of a theory, scientists usually do not change the hard core, but replace auxiliary hypotheses. This is called 'negative heuristics.' But when there are several rival research programmes in a field, this replacement of the protective belt should also lead to some novel predictions (this is called 'positive heuristics'). For, if a rival programme is more fertile than other programmes, scientists tend to choose this fertile one and to give up others. Lakatos' own account of novel prediction is just a temporal one, namely the prediction of totally new phenomena unthought of before, but for some reasons Frankel introduces a more complicated definition of novelty: "[a] fact is novel with respect to a given hypothesis and its research programme, if it is not similar to a fact which already has been used by members of the same research programme to support an hypothesis designed to solve the same problems as the hypothesis in question" (25, italics original).
Frankel finds that the history of the drift debate fits this Lakatos' account well. Frankel recognizes three research programmes in the drift debate (31). First, there are contractionists (CON), whose hard core says that the earth has been contracting periodically since its birth. Second, there are permanentists (PERM), whose hard core is that after the original settling of continents and oceans, they have remained relatively the same. Finally, Wegener's research programme (DRIFT) had the hard core that the continents have displaced themselves horizontally with respect to each other. They did change auxiliary hypotheses to meet predicaments. The final victory of DRIFT by Hess's hypothesis was due to the corroboration of a novel prediction made by the theory that the magnetic reversals should be symmetrical on either side of the ridges. So far, so good. But Frankel finds that the 'unchangeability thesis,' namely the thesis scientists never change the hard core of the programme, is undermined by this history. For example, the theories in DRIFT kept changing a part of the hard core of the programme, i.e. the mechanism of the continental drift. Similar changes can be found in CON. Frankel concludes that Lakatos needs to modify the unchangeability thesis and the account of the novelty to explain the plate tectonics revolution.
Frankel (1979b) tries a similar analysis from L. Laudan's point of view. Laudan's 'research tradition' is similar to Lakatos' 'research programme,' but different in several points (Frankel 1979b, 52-59). First, Laudan makes no rigid distinction between hard core and protective belt. Second, Laudan thinks that the acceptance of a theory is dependent on the problem-solving effectiveness of the theory. Laudan distinguishes conceptual problems and empirical problems, and divides empirical problems into three categories; solved problems (solved by this theory), unsolved problems (unsolved by none of the theories), and anomalous problems (solved by other theory but not by this theory). Scientists choose a theory by comparing the amount of solved problems and anomalous problems of each theory. Frankel argues that this Laudan's account fits with the case of plate tectonics better than Lakatos', if only Laudan takes Frankel's notion of novelty into account.
In a later paper, Frankel analyzes the strategies taken by scientists in detail (1987). Basically scientists try to increase the number of the solved problems of their own theory and to decrease that of rival theories. Frankel also provides an new account about how the plate tectonics theory closed the debate (241-243). Vine-Matthews-Morley hypothesis provided a time scale on the reversal of the geomagnetic polarity. But there are two other totally different ways to determine the same reversal time scale. A remarkable thing with Vine-Matthews-Morley hypothesis was that the time scale by this hypothesis showed exactly the same pattern as the other two measurements. Of course fixists have no explanation for the remarkable coincidence. This is why the scientists accepted the plate tectonics theory.
Let us now turn to R. Laudan. Her 1981 proposes a revision of the standard account of the revolution. This revision concerns the role played by the mechanism problem in the drift debate. As we saw, in the standard account by Hallam and others, Wegener failed because he could not provide a plausible mechanism for the continental drift, and Hess succeeded because he solved the mechanism problem. But according to R. Laudan this is inaccurate. First, when Wegener proposed the drift theory, the problem was much more serious than the standard account describes: "[t]he problem with drift was not simply that there was no known mechanism or cause, but that any conceivable mechanism would conflict with physical theory" (230, emphases original). Continental drift conflicted with the established geophysical view that the earth's interior is solid. But at the same time, the law of isostasy, which also conflicted with the solidity of the earth, was accepted because of the overwhelming evidence. So, Laudan concludes, if the other evidence for the drift theory was strong enough, the drift theory could be accepted without any conceivable cause. Second, when the plate tectonics theory was accepted, even though the kinetics of the plate movement was complete, the force that moves the plate was still unknown (235; see McKenzie's argument below). Rather, the plate tectonics theory was accepted because of the confirmations of its novel predictions. With these considerations, she denies the special status of the mechanism problem, and argues that novelty of prediction is much more important. This, of course, is in accord with the Lakatos' approach analyzed by Frankel, and R. Laudan recommends this approach with a revision similar to Frankel's, namely the denial of unchangeability of the hard core. In another paper, R. Laudan (1980) provides an interesting insight on the relation between research programmes and each scientist. In this paper she first points out that Lakatos cannot explain the development of the hard core of a programme. The reason Lakatos fails is, according to R. Laudan, that he assumes that each scientist is in a single research programme and therefore cannot question the hard core. But in this respect T.C. Chamberlin's 'method of multiple working hypotheses' describes the situation better (R. Laudan 1980, 333). According to this method, scientists pursue several different hypotheses at the same time before they decide their mind. In this way, we can cancel the biased stress of the advantage of the current working hypothesis. J.T. Wilson's career provides a nice case study of this method (R. Laudan 1980, 336-341). During the late 1950s and early 1960s, Wilson was working on three rival hypotheses simultaneously: the contraction theory, the expansion theory, and the convection current theory, which led Wilson to the basic idea of plate tectonics. Wilson could assess the strength and weakness of each research programme, and contributed the development of each.
R. Laudan and L. Laudan (1989) adds another interesting detail to this kind of approach. They pose three questions at the same time: why do scientists disagree?; why do scientists reach consensus?; why do scientists innovate new theory? Good answers to the first and the third questions tend to be bad answers to the second question. Their answer to these questions is that scientists are different in the strictness of the standards for acceptance of a theory (they call this phenomenon "disunity of method"; 223). Scientists disagree because of the difference of standards, and they reach a consensus when a theory meets the most strict standard. For Laudan and Laudan, the most strict standard is the confirmation of novel prediction. They argues that the drift debate agrees with this model.
Let us briefly analyze Frankel's and R. Laudan's arguments. Even though they stop talking about research programmes and research traditions in their recent works (see Frankel 1987 and Laudan and Laudan 1989), their works are fairly consistent in their approach. Some of the features of their arguments (emphasis on the novelty and denial of the unchangeability of the hard core) are also consistent. I think we can call these consistent parts the 'research programme' for their historical and philosophical research. And indeed this programme is very fertile, as their own works show. But there are several criticisms. First, Mareschal (1987) and Nunan (1984) criticizes Frankel's distinction of three research programmes as somewhat arbitrary. Contractionists and Permanentists were not conflicting programmes. Mareschal also stresses the extreme success of the fixist programs as an explanation of the rejection of Wegener's theory (Mareschal 1987, 195). In this view we do not need the lack of novel prediction as an explanation of the rejection. We will see Nunan's criticism on Frankel's account of novelty below. Kaiser (1993) criticizes Laudan and Laudan. According to Kaiser, disunity of method is not necessary for disagreement, because theory-ladenness of observation will do the job. Despite the theory-ladenness, enormous improvement of precision like sea-floor magnetism evidence can lead a consensus. We will see Kaiser's own position in some detail, also.
6. Evidence and confirmation
6.1. Geological evidence
Some geologists want explanations much more internal to the discipline. In this section we deal with two such geologists, McKenzie and Oreskes. D.P. McKenzie (1977), one of the first person who introduced the notion of 'plate' into geology, raises the question why the date of the proposal and acceptance of the plate tectonics theory is 1967 and "not at least fifty years earlier" (97). According to him, this is not a lack of imagination, but "the difference in behavior of continental and oceanic rocks when subject to deformation" (ibid.). The principal difference between the plate tectonics theory and former theories like continental drift or sea-floor spreading lies in the recognition of rigidity of the plate (100). This recognition enables us to exploit Euler's theorem for the mathematical treatment of kinematics without providing the mechanism of the continental drift or sea-floor spreading. The evidence of rigidity is particularly clear in the ocean. The positions of earthquakes concentrate on narrow lines and show the plate boundaries, and magnetizations of sea floors also show clear patterns. Neither of them have such clear patterns on continents. The similarity of the coast lines is a result of the rigidity of plate, but no one in the drift debate recognized the point. So there is no wonder the plate tectonics theory was not proposed before the development of oceanography. He also analyzes the reason Blackett and Runcorn's paleomagnetism failed to convince the majority (116-117). The reason is the complicated nature and specialist nature of the work. First, their conclusions depend on untested assumptions about the geomagnetic field in the past. Second, the magnetization of the rocks tells us the latitude of the place of the time, but not longitude. Because of these problems, the argument became complex and uncertain. And "unlike in physics, in the earth sciences long and complicated chains of reasoning are rarely correct" because there are so many factors which can influence on the validity of the reasoning (117). So it was reasonable for geologists not to buy the paleomagnetism. To sum up, what McKenzie claims is that the clear-cut evidence from the ocean was essential for the proposal and acceptance of the plate tectonics theory, because of the complex nature of geology.
N. Oreskes (1988) makes a similar point in a slightly different way. According to her, the evidence available in the 1920s and that in the 1960s are qualitatively different (340-341). In the 1920s, the evidence was homologies, i.e. similarity of patterns. These homologies are basically qualitative. On the other hand, the evidence used in the 1960s consists of geophysical measurements like remnant magnetism and computer based solutions of plate motions. The advocators of plate tectonics also used the old evidence used by Wegener, but only ex post facto. She calls this difference "an evidential split" (341). The homologies are too observer dependent, and this is why (at least in the U.S.) the drift theory was rejected (346).
Both McKenzie and Oreskes emphasize the importance of the quality of evidential support. Their conclusions have interesting implications especially to confirmation theories. So let us turn to perspectives from confirmation theorists next.
6.2. confirmation theories
Actually we cannot find many confirmation theorists in this field. Here, we look at Nunan's Bayesian analysis and Kaiser's kind of bootstrapping shortly.
R. Nunan (1984) proposes to modify the 'research programme' approach by Frankel using Bayesian analysis. As we saw in the section on Frankel, Lakatos' account emphasizes novel predictions by a theory. But it is not clear what exactly 'novel' prediction means. Nunan analyzes several candidates of novelty including the one Frankel proposes, and rejects all of them from Bayesian point of view. These are all "non-rational characteristic of human psychology to which we should not capitulate" (277). For example, he rejects Frankel's account because if the same fact is already used by a rival program (nothing in Frankel's account prohibits this), there is no reason that the supporter of the rival program are impressed with the 'novel' use of the fact in another program (278). So Nunan proposes an alternative account of novelty (279): "a fact is novel with respect to a given hypothesis if it has not already been used in support of or cannot readily be explained in terms of, a hypothesis entertained in some rival research program." The major difference between Nunan's and Frankel's accounts is that Frankel cares about only the theories in a single paradigm, while Nunan takes all theories into account (and Nunan's account is in accord with Bayesianism). If some fact is novel in Nunan's sense, it is also novel in Frankel's sense (not vice versa). Now, Nunan takes two cases from the continental drift debate, i.e. debate between Wegener and contractionists, and the debate between Hess's sea-floor spreading and Heezen's expansionism. the conclusion of Nunan's analysis is that some of the evidence found in the 1950s (and used in Hess's theory) was novel in his sense (301-302). This seems to be an unfavorable conclusion because the change did not occur before the confirmation of Vine-Matthews-Morley hypothesis in 1966. But the same argument applies to Frankel, because the evidence is novel in Frankel's sense, also (305). Nunan even finds that the evidence used by Wegener meets Frankel's account of novelty (306). With these considerations, Nunan concludes that his approach is better than Frankel's.
M. Kaiser (1991, 1993) provides a kind of bootstrapping approach. His favorite case is that of paleomagnetic evidence for polar wandering and continental drift. He analyzes the complicated flow of reasoning to decide the place of the north pole from the remnant magnetization. Just like McKenzie, he finds that the constructed evidence depends on theoretical knowledge, especially on the hypotheses of polar wandering and continental drift themselves (Kaiser 1991, 121-123). Kaiser concludes that this process can be best understood as a bootstrapping, namely the confirmation of parts of a theory using the theory itself. Kaiser (1993) develops his view in his reply to Laudan and Laudan (1989; see above). According to Kaiser, Laudan and Laudan overlook three points (Kaiser 1993, 508-510). First, the geological evidence available before the 1950s was heavily observer dependent, as Oreskes (1988) points out. Second, development of theories themselves was essential to make sense of the new evidence. Third, specialization of the subfields of earth science made the communication of new results difficult. In this situation, even though scientists agree upon the methodology, the confirmation becomes heavily theory-laden, and very few questions can settled instantly. This is why we find scientific debate and scientific innovation (Kaiser 1993, 510-511).
When we compare these two accounts by Nunan and Kaiser, apparently Kaiser's approach is closer to the geologists' own view expressed by McKenzie and Oreskes than Nunan's. But this does not mean that the Bayesian approach cannot deal with the problems described by McKenzie and Oreskes. For example, McKenzie's claim that in the earth sciences long and complicated chain of reasoning are rarely correct can be easily restated in probabilistic terms and incorporated in Bayesianism (though I do not want to spend time for this here). I could not find criticisms of their works in the literature, but apparently they should answer the challenges from two sides. One is from Lakatos' and L. Laudan's point of view, namely if these confirmation theories can provide overreaching account like their own ones. The other comes from sociological perspectives discussed in the next section.
7. Interests and biases
The positions discussed in sections 5 and 6 are all rationalistic, in the sense that they believe in the rational nature of a scientific theory choice. But there are views which try to introduce more social and psychological factors.
Stewart (1986, 1987, 1990) tries to analyze the plate tectonics revolution from a sociological point of view. He opposes rationalistic approaches because these approaches are dependent on the existence of uncontroversial observed 'facts,' which cannot be found in real scientific practices. Even the most crucial and decisive evidence for the plate tectonics theory, i.e. the Eltanin 19 profile, could be doubted; "Opdyke recounted: 'Heirtzeler said the Eltanin 19 profile was too perfect and caused by electrical currents in the upper mantle in order to get out of the Vine Matthews hypothesis'" (Glen 1982, 335; see also Stewart 1990, 133). Scientists' judgements are affected by their interests and other social factors. To reveal these social factors, Stewart uses a quantitative research on the correlations between several variables and expressed attitudes of geologists to the drift theory up to the 1950s (Stewart 1986). He finds several interesting correlations. First, the greater the number of publications before the expression of attitude, the more negative is the scientist's attitude to the drift theory. Second, the scientists familiar with Southern Hemisphere materials tend to support the drift theory. Finally, scientists trained outside of geoscience tend to support the drift theory. Stewart interprets the first and the third correlation in terms of their interest, namely 'investment in orthodoxy' as affecting factor (Stewart 1990, 232). As for the second correlation, he says that this "may indicate that such experience either forced the scientist to consider some or the most persuasive evidence or restricted the possible interpretations of the available evidence" (Stewart 1986, 271). It is not clear if he intends to say that this is a kind of interest or bias.
LeGrand (1988) also takes interest into account. He calls his position "eclectic" (13). On the one hand he agrees with L. Laudan in many respects, but on the other hand he is frustrated with L. Laudan's omission of 'interest' from the picture. In this respect LeGrand allies himself with sociologists. But by 'interest' LeGrand mainly means 'internal' interests, that is interests operating only in science, like struggle for authority and credibility (10). LeGrand's book uses this 'internal struggle' along with Laudan's model extensively, but let me just cite one case. When the Eltanin 19 profile was published, there was one alternative hypothesis that could explain the profile, i.e. Heezen and Carey's expansionism. Logically speaking the explanatory powers of the plate tectonics theory and expansionism were not so different. But expansionists were "few in number, lacked significant authority, and stature in the community and, perhaps most important, were inactive in the crucial years" (224). Expansionists lost in the 'internal struggle' because of these reasons.
R.N. Giere's (1988) decision theoretic approach is also worth mentioning. According to him, when scientists choose a model about the world, they evaluate the probabilities that the model fits the world best and that the rival model fits best, and consider the outcomes of each cases. If the overall outcome of choosing the model is satisfactory, scientists choose it. In the evaluation of outcome, different kinds of interests, like intellectual interests and social interests, come in indistinguishably (157-165). Giere applies this model to the drift debate (227-277). The outline of his argument is pretty simple. In the 1920s, few scientists had an interest in choosing the mobilist model, because it meant to throw away much professional knowledge before that (as R.T. Chamberlin's comment quoted by Hallam shows). The advocates of mobilism had special interests in the model mainly through their 'Gondowana experience' (the experience with the southern hemisphere materials used as evidence of drift). In the 1960s, scientists still had the interest against the mobilism, but new evidence increased the probability of the model remarkably and decreased the probability of stabilist model. This made mobilism a satisfactory option.
Finally, M. Solomon proposes the "social empiricism" approach (Solomon 1992, 1994a, 1994b). Social empiricism maintains that "social groups can work to attain and even recognize epistemic goal without individual rationality or individual cognizance of the overall epistemic situation" (Solomon 1994b, 219, emphasis original). From this point of view, Solomon enumerates five biasing factors influenced the decisions of geologists (Solomon 1994a, 333-334). First, geologists tended to evaluate evidence in their own specialty higher. Second, geologists gave their own findings especial weight. Third, prior attitude towards drift influenced the reception of data and arguments. Fourth, peers and people in power influenced the decisions of individuals (she cites Pitman's case; Glen 1982, 334-335). Fifth and finally, human interactions like the network of transmission of data or being invited to a specific conference plaed an important role. Many of the cases she uses are already mentioned by Stewart, LeGrand, and Giere. But her evaluation of these biases is strikingly different from theirs. She claims that these biases played a positive role for making a consensus for the empirically successful theory. For example, if geologists behaved totally rationally, it would have taken much longer time to form the consensus for the plate tectonics theory, and to eliminate the expansionist alternative (Solomon 1994a, 337-338). The point of this kind of analysis is in its normative application. This time biases worked very well. Then what we should learn is the appropriate distribution of biases to make sure such a success in the future (Solomon 1994b, 226-229).
We saw four different studies here. All of them uses the notion of 'interest' or 'bias,' but many of them combine this point of view with totally different approaches. I think that no one can deny that scientists' decision-making is affected by their interests, so the problem is how it is affected. Stewart's studies provide us with interesting sources to think about this problem. But I think that we can find much more rationality in geologists decision than Stewart suggests. His quantitative analysis allows various different interpretations, as Stewart himself admits (Stewart 1987). For me Giere's and Solomon's approaches in this respect are especially interesting. Giere is trying to provide a kind of unified theory of science, and Solomon is trying to reconcile rationality and irrationality by putting rationality at the society level. Of course there are problems. Thagard (1992) criticizes Giere because Giere's talk of probability is 'metaphorical' and his theory is hard to test (179). An apparent problem with Solomon is that she should show that these biasing factors are (or, at least, can be) distributed by some social mechanism. Otherwise the talk about rationality at the society level is nothing more than a metaphor. But these problems should be regarded as good touchstones to elaborate these theories rather than fatal flaws of these theories.
8. Concluding Remarks
There are several basic questions repeatedly asked in this literature. Was the revolutionary change in the 1960s continuous (Kitts, Ruse, etc.) or discontinuous (Wood, Frankel, etc.)? Did novelty play an important role (Frankel, R. Laudan, etc.) or were other factors like precision more important (McKenzie, Kaiser, Nunan, etc.)? Did social factors play an important role (Hallam, Stewart, Legrand etc.) or not (R. Laudan, Kaiser, Nunan, etc.)? As for continuity/discontinuity problem, my impression from the literature is that no one makes a good case for methodological discontinuity (see my comments in section 4). But some different sorts of discontinuity proposed by McKenzie and others seem to be reasonable. As for novelty, the plausibility of the importance of novelty comes from the remarkable confirmation of Vine-Matthews-Morley hypothesis and its (even more remarkable) effects on the geologists' community. But as Frankel (1987), Oreskes (1988), LeGrand (1988), and others show, there are various different plausible interpretations of the event. So I think too strong an emphasis on novelty like Laudan and Laudan (1989) is not warranted as it is. As for social factors, I think Stewart did a good job to show that at least some kinds of social factors are working in the debate. But I think that it is also true that rationality of scientists did play major role in this history. In this respect LeGrand, Giere, and Solomon make interesting suggestions for the reconciliation of these two factors.
Then, whose account of the history is the best? This is a difficult question, and my answer is heavily affected by my own 'internal interests.' The primary reason I study this history is to find some normatively useful generalizations. In this respect, the Kuhnian approach and a purely sociological approach are not suitable for my purpose. So I endorse approaches from confirmation theories and M. Solomon's approach because of their fertility as a source of normative application.
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