Reading Guide to: Kuhn, T (1977) The Essential Tension, Chicago: University of Chicago Press.
This book follows the more famous Structure of Scientific Revolutions, which is rich in historical example and detail. This is a more reflective commentary looking back on the success of that earlier book, and taking on some criticisms. It offers a more considered and thoughtful 'theoretical' commentary on the important concepts, such as paradigms.
I have left out a number of themes, including the constant an interesting parallels between the history of science as it is depicted here, and Piaget's theories of learning
We need to study science hermeneutically, for example to reconstruct Aristotle's context and culture in order to locate his thoughts and to get at his whole system, rather than trying to analyse particular concepts. Progress in science is made from a process of gestalt switch. There are some possible connections with the social milieu, but science is 'relatively insulated' from that milieu. Scientific communities should be the locus of research, and their connections with wider systems of education and communication.
Scientific revolutions occur in thought, usually preceded by some anomaly. Scientific anomalies can be explained, but, often, the explanation has implications itself which make other parts of theory problematic. Revolutions however are rare. More common is 'normal science', which involves mopping up problems, consolidating the position of previous work, and sometimes preparing the ground for new thought too (for example by whittling away areas that are undecided allowing anomalies to emerge, and sometimes even producing anomalies directly).
Normal science consists of 'puzzle solving', and this leads us to the concept of paradigm. A paradigm consists of basic concepts (such as 'force'), but these are never defined explicitly. Instead, they are demonstrated by teaching various standard examples, which avoids speculating about difficult and debatable definitions. Paradigms therefore are best seen as the standard examples which produce solutions to similarly conceived problems. Paradigms can be expanded through the publication of books into a whole world view of a scientific community. Science is therefore a group product, and groups are held together by value systems. These value systems need not be total, explicit, or even free of conflict, and they're not simply deterministic. The commitments to normal science and are acquired through the use of specialist language and the application of paradigms to nature: the incommensurability of paradigms is best seen as a translation problem.
This has a particularly good discussion on the subjective elements of causal explanations, although I have not recorded detailed notes on it here.
There are problems in establishing exactly when discoveries are made, and the usual approach is to identify individuals as responsible. This is naively individualistic. The argument is best developed by looking at discoveries which appear to be novel, that is not predictable in advance by existing theory. Take the example of the discovery of oxygen:
(a) Bayen produced a gas by heating the red precipitate of mercury. He called this gas 'fixed air', and it was carbon dioxide.
(b) Later, Priestley performed the same experiment, and this time noticed that objects will burn in the gas that was released, and he called this 'nitrous air'. It was nitrous oxide.
(c) Priestley told Lavoisier of his results, and he repeated the experiment which led to more tests of the gases that were released, and the discovery of 'pure air' .
(d) Priestley repeated the experiments himself and discovered 'dephlogisticated air'.
(e) This led to more work by Lavoisier, who eventually concentrated the gas (oxygen) as a separate component of air.
At which stage was oxygen actually discovered? At this stage of obtaining a pure sample? But Priestley did that at stage (d), although he wrongly identified what he had got. Even Lavoisier, who had the right identification, had not got this theory developed by this time, so there was a gap between his observations and the existing theoretical explanations. A similar story can be told about the discovery of Uranus. The object was originally spotted by Herschel, but wrongly identified as a comet (and before that as a star). Only when it failed to behave as a comet was it identified as a planet. X-rays offer similar complexities: their effects were seen before Roentgen, and his contribution was to see these effects as a result of a new kind of radiation.
What these brief accounts all show is:
(1) There has to be an experimental isolation of an anomaly
(2) This is usually accidental, and has often happened before as well, sometimes as a by-product of standard work
(3) Some individual recognises the event as an anomaly specifically
(4) Various instruments and concepts have been developed to such a state that a violation of expectations becomes noticeable
(5) The anomaly leads to further conceptualisation, a pursuit of the problem
(6) The discovery is unexpected and react back on existing theory. Thus Herschel's discovery prompted new investigations and disrupted the old view of the solar system, permitting further discoveries. Roentgen's discovery led to rethinking the old cathode ray experiments which had failed to control the effects of X-rays, the development of new instruments, and thus the discovery of more new types of radiation. The discovery of oxygen leads not only to the discovery of new gases but to a new theory of combustion [in his earlier work, Kuhn points out that the old theory of combustion was by no means immediately displaced, however. The debate between phlogiston and oxygen theories of combustion lasted more less until the death of Priestley].
Measurement in science has an important role, but historical investigation shows some interesting points:
(a) Measurements never agree exactly with predictions. Instead, there is an acceptable range of error, although this changes. Thus quite large discrepancies between observations and theory were acceptable for the Ptolemaic school, but were concerned as signs of a crisis for Copernicus.
(b) Measurement is an important part of experimental technique, especially important for the mopping-up operations of normal science. However, it is not always easy to resolve disputes or extend theories by measurement -- some implications of the work of both Newton and Einstein were very difficult to actualise and measure. In these cases, scientists tend to offer instead of precise measurement: a belief in the theory's potential; acceptable approximations; examples of one successful case of experiment (one observation of bending light waves served to buttress faith in Einstein).
(c) As precision in measurement develops, anomalies are more likely to arise -- but, as the examples above show, failure in measurement does not usually constitute an anomaly itself.
(d) Measurement does not offer an independent test of theories, since measurement is guided by theory. Effective measurement is often defined as enabling some correspondence between observations and predictions to occur. Any discrepancies usually lead to new measurement techniques rather than new theories. Thus 'application' of theory very rarely leads to new theories, since experimental data often arises from theory in the ways described. Further, sometimes different theories can fit the same data (and so data cannot be used to decide between theories).
(e) Measurement is useful where there is a theoretical crisis, where anomalies arise, but many inconvenient measurements are bypassed and seen as error. This is not a purely rational process -- interesting 'errors' might be pursued if the effects are outside the normal range, or if the data is repeatable, or even if the results intrigue the experimenter. Sometimes, such data can be seen as an error which will be resolved by better techniques, sometimes a theoretical system can persist despite an anomaly -- thus the erratic orbit of Mercury was an anomaly for Newtonian physics for years. Thus anomalies do not arise only through measurement: sometimes a new technique or a new instrument will throw up incompatible data, but this must be seen as somehow contrary in a fundamental way for the background theory if it is to develop into an anomaly.
(f) There needs to be new theoretical work as well, and this always arises from some subjective recognition of faults with the old theory. A crisis therefore may lead to new empirical discoveries as prerequisites for theoretical ones. However, the crisis is usually fought off. Quantitative anomalies are the hardest to resist, since qualitative problems can be easily fudged -- for example, phlogiston is supposed to escape from metals when they are heated, but some metals apparently gained weight; the phlogiston men simply invented various ad hoc hypotheses such as that phlogiston must have negative weight; effective quantitative techniques were able to show how much weight had been gained and from where.
However, anomalies alone are insufficient, and there must be a new theory available to replace the old one. Measurement is therefore best in helping to choose between theories, and court stated accuracy is often preferred even to qualitative loss (an example of such loss is provided by Newton's theory of gravity which abandoned the question of the origins of gravity). Overall, quantification is very useful in processes of professional verification and in the problem of selection of theories, but it arises only with considerable efforts to theorise and in connection with other factors affecting choice.
In an appendix to this chapter, Kuhn discusses social sciences. Briefly, there can only be effective and productive anomalies if there is an organised set of expectations and some prior theoretical consensus. Natural sciences meet these conditions, but social sciences do not: there is still substantial disagreement about techniques and paradigms [and thus it is very unlikely that decisive enough anomalies can arise to help us move from one 'perspective' to another].
Convergent thinking plays a crucial role in the development of natural science -- divergent thinking is only useful if there is some theoretical crisis. There are extended periods of normal science which require convergent thinking. A great scientist has to converge, and commit themselves to normal science -- and be prepared to consider revolutionary and divergent thinking as well. The same goes for scientific communities. Convergent thinking is encouraged and the way which science is taught, in the development of 'mental sets' [which is usually one area in which science teaching has been condemned by progressives -- but Kuhn sees the importance of convergent thinking]. Convergent thinking can produce innovations. Indeed, progress proceeds through a set of alternative consensuses, not by holding a series of competing approaches at the same time. Convergent thinking helps the scientific community focus on problems. There must be some agreed background theory when approaching a new field. Further, no one investigates puzzles unless they are sure initially that they can be solved by current theory. Theory guides us to non-trivial anomalies.
Of course, agreed theories must be potentially flexible. Kuhn shifts to examine the 'personality characteristics' of revolutionary thinkers at this point. In an appendix to this chapter, he also considers the role of 'external social forces' in assisting scientific convergence [not very well -- he hints that these forces supply problems for the scientific community, but gives no details]. He seems to be arguing that basic science, or the selection of mere theoretical puzzles, is often inadequate to solve these external problems. This failure to deliver provides some social space for innovators, who are classically marginal to scientific communities anyway [a theme taken up in the earlier book].
This focuses on the debate between Kuhn and one of his main rivals Popper. The two thinkers have much in common, since both denied that size makes progress by accretion, both see a role for revolutionary change, both stress the disparities between observations and theory, and both emphasise the role of scientific tradition. But Kuhn says there are some differences too, over matters such as the role of tradition, or the role of falsification. There are also more fundamental differences in the whole gestalts of the two:
(1) Statements and hypotheses are most commonly tested within normal science for Kuhn, relying on scientific tradition, and operating mostly as puzzle solving. For Popper, the focus is on problems with the whole tradition, what Kuhn would call anomalies, and here what is tested is the ingenuity of the individual great thinker rather than a paradigm.
(2) Popper's revolutionary overthrows are very rare for Kuhn, and only where there is some prior crisis. They are not characteristic of most science, and can only take place in conditions of extensive normal science.
(3) Normal science offers the criterion of demarcation [between proper science and its rivals, such as astrology], rather than attempts at revolutionary falsification. Normal science is essential for progress, as we have seen, unlike premature sciences where there are competing consensuses. For Kuhn, you only get a science where critical philosophical discourses have been abandoned! Popper's criteria of theory choice [roughly, that only science is falsifiable, and that falsification leads to revolutionary overthrow] are really criteria to guide the choice of metaphysical systems [that is, philosophical theories of science rather than science itself].
(4) Testing is rarely decisive. Decisive tests arise only after frequent unsuccessful attempt to resolve puzzles as above, and they must be rooted in a background tradition. Thus astrology is not a science, but not because it is so vague as to be unfalsifiable (Popper's position), but rather because its failures of prediction have no theoretical implications: because there are so many uncontrollable and difficult to determine variables, such as the need to ascertain the exact date of birth, the theory can always survive a lack of successful prediction. In this way, the explanation of the failure of prediction is actually quite 'scientific' in astrology, and there is a parallel with the way in which 'measurement problems'are sometimes used to explain the lack of predictive power in natural sciences. Astrology, like psychoanalysis and medicine, is unscientific because it is a craft, based on a general theory which lends plausibility, but which is not precise enough to reveal anomalies. Indeed there are no puzzles either, hence no research and therefore no science. As a result, Popper's demarcation criterion needs revision. A science has conclusions which are logically derivable from shared premises, but in a specific form rather than a general one. Even here though, the specific form is only a sufficient condition: other sciences have precise and specific conclusions even if they are not logically derivable.
(5) Theories are often replaced before there is a decisive test. For example, Copernican replaced Ptolemaic systems before any decisive testing of the theory. It was simply that the Ptolemaic system had ceased to provide puzzles [earlier, Kuhn argues something similar for astrology].
(6) Science shows itself to be capable of learning from mistakes, but what exactly is a mistake? Individual mistakes are only identifiable set against group practices which help to isolate them. Community mistakes are more difficult. The Ptolemaic system was not a 'mistake' but a different gestalt. It takes a particular kind of mistake, an anomaly, to infect a whole system. It is therefore wrong to use procedures where individualsdo research to describe changes of whole systems: Popper assumes that theories change according to some undoubted techniques whereby mistakes are rectified, but this arises from a confusion between normal and revolutionary science.
(7) There is a logical asymmetry in Popper's theory of falsification [Popper had used this argument to defeat the inductivist view of science, whereby evidence is sought to confirm theories. Popper argues that no amount of confirming incidents can logically prove a theory, whereas one single significant case of this confirmation can falsify it]. In Kuhn's view, an anomaly arises where something has failed to be accounted for by a theory, but falsification or refutation implies a formal, completely certain and unaccountable compulsion based on assent. Not so for anomalies, which show that theories can be endlessly reformulated or 'ad hoced' in an attempt to fight off negative implications. This is indeed recognised by Popper, but he gives us no guidelines to account for falsification episodes. If we examine his work on demarcation, we find a theory is scientific if and only if it includes 'observation statements' (especially those singular existential statements which refer to the simple presence or absence of objects). These have to be deducible from the theory, for Popper, not actual observations themselves. If observation statements are crucial to falsification, then logical disproofs are also available [for example, the scientific community can be asked to agree whether or not a bending is detectable in light].
However, Kuhn wants to question whether scientific theories can ever be cast in this form, and even if so whether this will describe the actual logic of scientific knowledge. Popper seems to want to talk of knowledge as something empirical, so that real observations can provide falsifiers, but the problem remains -- when does logic alone require the scientist to abandon the hypothesis? Popper's work is really a description of the ideology of science rather than its practice, a description of procedural maxims rather than actual methodological rules.
There are problems with Popper's notion of verisimilitude too. If theories are formulated so that the logical consequence is that they can be falsified, this assumes that there is no revolutionary change in background knowledge. In other words, this implies a full articulation of scientific knowledge, and definite, agreed rules of application: in other words it implies 'normal science', indeed, normal science without any puzzles.
(8) There are non-logical elements involved in falsification, such as shared recognitions and learned classifications. These are often held implicitly, and generalised explicitly only if there are specific problems to be solved [coons example here includes problems of teaching science]. Falsification therefore involves a theoretical and psychological decision to infer problems of classification from an observation. Scientists have to be prepared to make a risky explicit definition, must just does not square with the usual pragmatic uses of theory. Scientific criteria are defined with definite cases in mind, and it is only when something unexpected occurs to science do they become problems. Even then, different consequences arise from these problems, not guided by logic alone.
(9) So how are we to explain change in scientific theories? It is not a logical process alone, although there is sometimes a logical component, often subsequently. There is no logical or rational theory choice. The actual process is still largely unknown, although there are hints that the evolution of a profession might be an important process. Scientists largely prefer their gains yielded by quantitative solutions to puzzles, although they sometimes do exclude problems or leave them open. Is the unification of theory a professional goal? Explanatory power certainly does seem to be a major goal, but explanation is psychological and sociological, involving an account of a value system or ideology, and the development of institutions to transmit it. Thus the approval of fellow scientists is a major motivator for those trying to solve puzzles [Kuhn suggests it is more important than any actual practical outcome -- see Lyotard on the decline of the 'performativity criterion']. How group unanimity is secured and maintained is the main question.
Despite Popper's denials and his emphasis on logic, science is 'subjective' after all. Popper half recognises this himself, especially if we see his prescriptions as moral imperatives for scientists rather than as descriptions of actual procedures.
This chapter contains some 'second thoughts on paradigms'. The term was used in different senses in the earlier Structure of Scientific Revolutions, mostly in two main senses -- to describe the global commitments of the scientific group, and to describe the commitments of subsets within the overall group. The two were confused, in terms of describing, for example, the pre-paradigms stage (now the different schools in the pre-paradigm stage can have paradigms themselves). Scientific communities need to be researched first, as a series of social networks [instead of formal analyses of paradigms]. Variability will occur, largely according to the practices of scientific specialities, the extent of their shared goals, the state of the education system, the existence of for communication among members, extent of consensus among them, and the importance of shared references in classic texts. Such commitment can take place at different levels as well. In order to manage this complexity, Kuhn suggests that we replace the term paradigm with the term 'disciplinary matrix', and focus on selected aspects of this matrix ( symbolic generalisations, models and exemplars) :
Symbolic generalisations, which are very important for logical and mathematical operations, the existence or absence of which can also confer prestige. These generalisations may appear in different guises -- for example as 'laws', more usually as 'law - sketches'. In these cases, empirical contents affect generalisations from the beginning. Laws may be shaped by notions of elegance, or tacit knowledge, and these criteria are taught through characteristic problem-solving exercises. Such laws are usually 'attached to nature', not by deploying some definite, logical object language, but via operational rules or through some notion of 'correspondence'. [Kuhn agrees that scientists may share the belief that somehow correct usage of these rules delivers this correspondence, which is more less what Adorno says about the magical use of scientific rituals]. The whole process is implicit, and scientists have largely abandoned 'sense datum language' for 'basic language' as a form of operationalism. Although such statements can be formalised, the basic problem remains unanalysed -- how to basic statements get attached to nature?
Are scientific statements like this really tautologies or empirical statements? Laws or definitions? The problems are glossed by teaching science and by practising it: this is how scientists simply 'recognise' some correspondence between a theorem and some actual examples, almost as a matter of selective perception. Analogies are involved. Indeed, using analogies can lead to progress, as different analogies have different implications -- thus Galileo saw the motion of a pendulum as analogous to that of a rolling ball. [If I remember the discussion in the earlier book, pendula were seen before Galileo as falling bodies]. Thus 'group - licenced resemblances' lie at the heart of correspondences between theories and nature. Examplars are the main device to share these. Perceptions and gestalts come first, and only then are explicit criteria are referenced, if at all.
Data is usually seen as what is given to experience. 'Basic statements' play an important role, as we have seen [remember that these are simple existential statements -- that something exists]. However our sensations as such are not immediate and given. A good deal of processing of stimuli is required, and there is no 1:1 relationship between stimuli and sensations. Scientists have to learn procedures here, and these are shared in scientific communities. Kuhn accepts that this means there are literally different worlds. Learning takes place primarily from ostentation [showing people what things mean] and feedback, and is intended to help people identify suitable discriminations. It is these discriminations that lead to different data. There are no definite correspondence rules, although symbolic generalisations are useful. Indeed, it can be unhelpful to be too explicit about these correspondence rules, since this exercise may weaken the communities' cognition. Boundary disputes are inevitable but are usually dealt with by compromise rather than logical choice. Fixed rules are unnecessary and can be unhelpful, and what is better is a recognition that learned perceptions of similarity are more useful: this can allow the exploration of analogies.
In conclusion to this chapter, we can now dispense with the term 'paradigm' altogether, as long as we agree that the main feature of science is its peculiar process of learning its procedures.
This deals with objectivity, value judgments and theory choice. Paradigm shift is not simply a matter of logical proof but a matter of argument and persuasion. Progress takes place through collective decisions to prefer one rather than another. The exercise is rhetorical, but there are some shared criteria of good theory:
(1) Accuracy is to be preferred, providing some measure of agreement about deductions and observations
(2) Consistency, both internally and externally
(3) Broad explanatory power, so that a good theory has many consequences
(4) Good theories are simple and unifying
(5) Good theories are fruitful
There are difficulties with each of these, however, for example each criterion can be vague and they may contradict with each other, as could (1) and (3), for example. Turning to actual examples, the Copernican system was not more accurate than the Ptolemaic one until Kepler was able to devise more precise measurements. There are different problems as well -- for example oxygen theories give more accurate readings of the weight relations in reactions, but phlogiston theories give a more accurate account of the similarities between metals and the dissimilarities between ores. Both Copernicus and Ptolemy were consistent, but with different background knowledges, and neither was really simpler in usual senses.
Choice is clearly influenced by other criteria. For example, Kepler was influenced by the neo-Platonic movement, Darwinism became acceptable because it resonated with nineteenth-century British social thought. Personality factors are important too, such as willingness to accept risk. These are accepted by historians as important but subsequently ignored by philosophers:
(a) Philosophers have a belief in the development of a full logical algorithm for theory choice, with the subjective elements as variables that have not yet been controlled. But this is an unattainable ideal
(b) Subjective elements are acceptable as affecting the discovery process, but are seen as having nothing to do with subsequent justifications, such as testing, which has to be 'objective'. There are lots of examples to the contrary however. Pedagogy has a more important role than justification procedures; crucial experiments take place typically after the scientific community is convinced; each decision has a context -- for example, some solutions are seen as more powerful and are therefore preferred.
(c) Even if there is some sort of algorithm, there are often different possible candidates for theoretical explanation. The increasing unanimity which develops among scientists is not explained solely by some emergent logical and objective process of theory choice.
(d) The criteria cannot be simply universal and compelling, or no puzzles or disagreement would arise. Scientists operate with vague norms or maxims rather than rigorous criteria, and these are affected by value systems. Social utility is often an important consideration, for example. Further, allowing disagreement is an important professional value, and maybe the only way to produce new research.
(e) Progress is as mysterious a process as induction [another dig at Popper]. No one has a full explanation. The vagueness of scientific rules permit 'normal curve interpretations' [that is, probabilistic ones?]. This leads to an argument for the growth of large scientific communities and the toleration of individual freedom, at least as minimal requirements. The social milieu is again denied as an important determinant.
Overall, the traditional criteria listed above ( 1 to 5) might well be permanent, but the value attached to them varies, and each can assume different applications and different weights. For example, accuracy now offers a means of quantitative agreement in all sciences, whereas once it was important only in astronomy. Utility was much more important in the past for chemists rather than mathematicians. There has been there gradual removal of questions of qualitative accuracy (for example, the oxygen theory of combustion abandoned any attempts to explain the colour, texture or other qualities of the substances involved).
Terms like 'subjective' and 'objective' need clarification. They are clearly interlinked, but we are accustomed to call judgments 'subjective' if they involve matters like mere aesthetics. The term implies that judgments are non-discussable. The interesting thing about scientific judgments is that they include subjective elements but they are usually also the focus of considerable discussions.
Finally, there is inevitably partial communication between the advocates of different theories. Each advocate tends to appeal to his own ground, and words function differently in each system. As a result, 'choice' is often more like a conversion than a logical decision. Results do help to persuade, of course and investigation of results is often a key way to develop familiarity with the new language.