Philosophy of Science - Resources

Proliferation

Sun, 13 Jun 2010 11:31:49 +0000

By Paul Newall (2005)

Arguments for proliferation as a methodological principle are often associated with the philosopher of science Paul Feyerabend (1999) but they date back at least to J.S. Mill (1869 [1991]) and take the same form.

In the latter’s On Liberty of 1869, four reasons were given to advocate proliferation of theories and "forms of life".

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First, if any opinion is compelled to silence, that opinion may, for aught we can certainly know, be true. To deny this is to assume our own infallibility.

The history of science is (often unfortunately) littered with examples of theories that were true without doubt and yet crumbled all the same in spite of this certainty. Although case studies such as the so-called Galileo Affair have shown that the relationship between early science and religious strictures was considerably more nuanced than had previously been believed, such that the claim that science was "held back" by religion is problematic, nevertheless the assumption of infallibility has consequences for the speed with which we can discover an error. After all, why question a surety? It has tended to take people with extreme tenacity like Galileo to adduce doubt when there is little reason to do so before the erroneous nature of the certainty can eventually become clear, of which more below.

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Secondly, though the silenced opinion be an error, it may, and very commonly does, contain a portion of truth; and since the general or prevailing opinion on any subject is rarely or never the whole truth, it is only by the collision of adverse opinions that the remainder of the truth has any chance of being supplied.

It is now straightforwardly accepted that science is a fallible venture, such that our theories are never certain and are always assumed to contain some errors (although obtaining this admission where it pays in rhetorical terms not to mention it is sometimes a painful process). Given that this is so, we can take two points from Mill's remarks: firstly, that although other theories may be flawed they may still be partly true (or possess some degree of verisimilitude, or truthlikeness); and, secondly, that by bringing theories together that conflict in some or all areas we can use one to identify the flaws in the other, and vice versa.

Indeed, this "collision of adverse opinions" is for Mill an important means by which to come by knowledge. Even where an opinion strikes us as deluded or wholly ignorant, the very process of setting out why can be beneficial because it forces us to rehearse the reasons and hence to understand how a theory comes to be considered false rather than relying on an insistence that only a fool would think otherwise. This leads us to the next reason:

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Thirdly, even if the received opinion be not only true, but the whole truth; unless it is suffered to be, and actually is, vigorously and earnestly contested, it will, by most of those who receive it, be held in the manner of a prejudice, with little comprehension or feeling of its rational grounds.

Here Mill insists that this business of contesting ideas – no matter how sure we are of them – is valuable insofar as it prevents us holding them without appreciating why they were thought worthwhile originally. There is more, though:

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And not only this, but, fourthly, the meaning of the doctrine itself will be in danger of being lost, or enfeebled, and deprived of its vital effect on the character and conduct: the dogma becoming a mere formal profession, inefficacious for good, but cumbering the ground, and preventing the growth of any real and heartfelt conviction, from reason or personal experience.

Not only can an idea unrehearsed become held as a dogma, then, but this state of affairs can also prove a hindrance to further development, whether of the idea in question or others simultaneously or subsequently. It is here that we arrive at the full meaning of Mill's advocacy of pluralism and proliferation: even the best ideas can be improved by their clashing with others, even poor ones, because they are either enriched by their own flaws being highlighted or revealed, or else because the challenge leaves them untouched but better understood, forcing us to articulate them more clearly and to not insist upon them due to the power, prestige or authority of their supporters. Conversely, there is no value in even a true idea that is not continually subjected to challenge by even apparently false ones. Moreover, it has often been the case that the more sure of a theory people have been, the less inclined they are to question its anomalies or continue to work on its development.

One consequence of the principle of proliferation that may not be immediately apparent from Mill's discussion was elaborated upon by Feyerabend and is that these so-called "poor ideas" cannot be dismissed for the very same reasons that the "good ideas" cannot be accepted uncritically. Not only is the question of demarcating between good and bad ideas a thorny one itself, but the good ones typically started life as bad and those they replaced provide them with much of their content through the process of improvement. Any student of the history of science is also familiar with numerous examples of ostensibly hopeless theories that were regarded with scorn by all right-thinking people only to make a comeback (on several occasions in some instances, like atomism), such that it would eventually be thought preposterous that anyone would have imagined otherwise. At the time of Copernicus, say, the arguments marshalled by the Aristotelians against heliocentrism and geokineticism were so strong that Galileo had to appeal to reason over and above the clear evidence of the senses in order to explain why anyone should doubt geocentrism and geostaticism. This is not to say that a theory will make a triumphant return, of course, but only that it might and that, in the meantime, by keeping it in mind we remain aware why we (tentatively) hold to an improvement on it.

Another reason to be interested in proliferation is that theory choice is no longer accepted to be a simple matter of agreement with the evidence. The importance of rhetoric, as well as social, political, economic and thematic factors, amongst others, means that the current superior status of one theory is insufficient grounds for supposing that this circumstance is due solely to the merits of the victor (and here Lysenkoism in the former Soviet Union is perhaps the most chilling example of a theory that succeeded thanks to ideology and at the cost of many lives). Notice also that this situating of theories within a wider context is unavoidable: all the models and ideas we develop have some beneficial aspects or we would not come up with them at all, but the questions are to whom and to what end? Where only one option exists we have no opportunity for comparison and hence no way of knowing whether we have the best of the matter.

Indeed, it can happen that a theory is incorrect in an important way but there is no experimental way of knowing this. An example discussed elsewhere concerns the phenomenological theory of gases, which was replaced by the kinetic theory thanks to Einstein's Investigations on the Theory of Brownian Movement. In this case the consideration of an alternative theory in spite of there being no experimental falsification allowed Einstein to explain the same situation with a new theory that led to novel predictions, which turned the tide against the phenomenological theory and replace it with the kinetic.

Arguments against proliferation have taken several forms. One important and wider issue is that pluralism runs contrary to one of the prevalent thematic ideals: the search for unity that runs through much of physics. From this perspective, it makes little sense to proliferate theories when the aim of science is (or should be) a small number of laws that can account for all phenomena. At base this approach relies on the same notion that both Galileo and the Church insisted upon; namely, that the truth is singular and hence even if our theories may be fallible they are still getting closer and closer to one reality. Methodologically speaking, then, the suggestion is that we should not be hearking back to old, defeated theories but concentrating on the best we have and striving to improve them. In particular, our best theories (such as evolution or quantum mechanics) may be incomplete but it is unthinkable that they could be discarded at some point in the future, so we should work on the few remaining details and not concern ourselves with alternatives just to satisfy otherwise sound advice on understanding ideas.

Notwithstanding that many theories in the past were in precisely this situation (consider the certainty with which Copernicus' writing was rejected, for instance), it is here that Feyerabend's argument applies. This singular approach presupposes that our theories can be straightforwardly developed by further application but the example of Brownian motion shows that sometimes this is not possible. More generally, if a theory T1 predicts circumstances C1 but what actually occurs is C2, even though C2 is (currently) experimentally indistinguishable from C1, then we have no reason to look at alternatives to T1 in spite of it being incorrect. If we instead proliferate theories and find that some T2 predicts C2 then we have a justification for trying to experimentally differentiate the two or, where this remains impossible, for studying the merits of the two otherwise. Another possibility, of course, is that the investigation of T2 allows us to tweak T1 slightly such that it does predict C2 while maintaining its other advantages. In this way proliferation leads to strengthening or deepening the content of theories.

For Mill's part, he was very clear on why it can never suffice to rest content with one theory:

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He who knows only his own side of the case, knows little of that. His reasons may be good, and no one may have been able to refute them. But if he is equally unable to refute the reasons on the opposite side; if he does not so much as know what they are, he has no ground for preferring either opinion.

On this view, it is never enough to know a theory inside out; we also need to understand why alternatives exist, why they are believed to be true and why they fail in order to appreciate the value of the theory as an improvement or more deserving of our attention. The clash between advocates and deniers of the phenomenon of global warming, for example, has pushed both sides to reconsider their arguments and strengthen them, allowing flaws to be amplified (although political and other pressures are such that a good argument is rarely enough to change a policy), while the challenge of creationism and the elaboration of intelligent design have forced biologists to enter the public arena and explain why evolutionary theory is so highly confirmed and the foundation of biology.

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Nor is it enough that he should hear the arguments of adversaries from his own teachers, presented as they state them, and accompanied by what they offer as refutations. That is not the way to do justice to the arguments, or bring them into real contact with his own mind. He must be able to hear them from persons who actually believe them; who defend them in earnest, and do their very utmost for them. He must know them in their most plausible and persuasive form; he must feel the whole force of the difficulty which the true view of the subject has to encounter and dispose of; else he will never really possess himself of the portion of truth which meets and removes that difficulty.

Here Mill goes further, insisting that not only do "the arguments of adversaries" deserve to be heard just as part of learning about the superiority of the current theory but rather in their very strongest form. This is no recommendation of a superficial treatment, then, but a conviction that by supporting and developing alternatives we contribute to the improvement of our knowledge, even where these alternatives achieve nothing when considered in isolation. This is to say that a theory may be preposterous on its own but becomes of benefit to us when taken as providing an ever-present challenge to others. It goes without saying that the stronger it is, the greater our confidence can be that our current ideas have survived critique.

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So essential is this discipline to a real understanding of moral and human subjects, that if opponents of all important truths do not exist, it is indispensable to imagine them, and supply them with the strongest arguments which the most skilful devil's advocate can conjure up.

It was this last principle that Feyerabend embodied, even though there are always enough people who will paint those who apparently depart from orthodoxy as heretics by implication or opponents of clear thinking. On the contrary, it is the effort to expound, support and defend arguments we do not agree with that allows us to truly understand them enough to dissent and prefer an alternative. Proliferation enjoins upon us both a methodological pluralism and a belief that a theory is of no value unless subject to a continuous process of challenge, of which even the most dismissed of ideas is an indispensable part.

Another objection to proliferation – often the most common – is that it may be a good idea in the abstract but not in practice. Unfortunately for scientists and vacuum cleaner salesmen alike, there is only so much money to go around and hence we cannot afford to allocate resources to any and all ideas that come along. A theory can be challenged by a well-developed and plausible alternative, in keeping with the argument so far, but little or nothing is to be gained (indeed, it would even be detrimental) by taking funding from our best theories to support hopeless substitutes.

The first point to note about this rejoinder is that it effectively begs the question against the alternatives: if we deny support to an idea we can hardly criticise it later for being undeveloped and not worthy of consideration. Theories start their lives riddled with internal contradictions and partial (or even complete) disagreement with the evidence but over time may – or may not – prove their worth and begin to be taken seriously. Perhaps it is because this process of acceptance is usually slow (even where so-called "revolutions" in science are taken to have occurred, a claim that is increasingly untenable in historiographic terms) that we fail to notice it and forget that there were times when our best theories were themselves rejected as absurd or unlikely? Rejecting an idea because it is prima facie false would thus have been catastrophic methodological advice for science in the past and there is no reason to think otherwise today unless we presuppose that the current state of science and knowledge is approximately the final one, a conceit that seems to affect all ages.

What is also ignored in this response is that an idea is not only credible in proportion to how much work has been done on it and how much money is behind it. The early quantum theory was rejected with a considerable measure of displeasure by some physicists (Heisenberg told Pauli in a letter of 1926 that "[t]he more I ponder the physical part of Schroedinger's theory, the more disgusting it appears to me" (p.15 in Holton, 1988)) because it disagreed strongly with their thematic preferences, while the notion that there is or is not a higher intelligence involved in the creation or sustaining of the universe is no less unpalatable to some. Moreover, there are power structures involved in science just as anywhere else and those who have an investment in the prestige and financial rewards associated with a successful theory may not be as open to new ideas and the redistribution of funding when appropriate as their claims to the contrary might suggest. Money is thrown at projects with little or no chance of success (for example, missile defence systems) or no proven achievements (such as string theory) not because of some inherent value but because the rhetoric or personalities behind them do a better job of convincing others, while a skilful synthesis can create unity where there was none (Dobzhansky's in evolutionary biology, say) or a consensus can be constructed (like the usage of the DSM in psychiatry). Insisting that time and funding are limited, then, ignores their already unequal distribution and that the relative status of a theory is determined by far more than its empirical support. That the decision between theories is complex and based on many factors, some of them extra-scientific, is no reason to restrict our efforts to few or ignore the arguments for proliferation.

Tempering this realisation is the frequent (and necessary, for Feyerabend) association of proliferation with tenacity, the tendency of scientists (and people in all walks of life) to persist with their ideas even in the face of the most adverse of difficulties. Once again, the history of science is replete with examples of theories or conjectures that by all methodological standards in use should have been discarded but were maintained in spite of experimental results to the contrary or the most grievous of conceptual problems (see the discussion of falsificationism for more instances). Perhaps the finest illustration of tenacity – and its link with thematic commitment – is provided by Einstein's response to the question of how he would have felt if Eddington's expedition of 1919 had failed to confirm his theory of general relativity: "... then I would have been sorry for the dear Lord - the theory is correct."

The coupling of proliferation and tenacity thus goes some way to assuaging the concerns of those who would prefer not to waste time on what they consider to be bad ideas. As Mill noted, proliferation requires that we work with the strongest possible version of defeated theories in order to better our own, and vice versa, and the way to achieve this is to ensure we persist with both even when all seems lost or when it would be absurd to withhold assent that a theory is correct. This is not to say that no division of labour can be employed and that we each have to consider every idea in the marketplace, but only that it is in our interest to see that those who wish to study them are able to. This means that scientists working on a theory do not have to reassign part of their time to develop alternatives in the name of proliferation but that we should not condemn these alternatives out of hand. They may compete for funding, of course, just as we would expect given the parallel principle of tenacity, but we should view their rhetoric and behaviour in these terms rather than as indicative of a neutral claim to superiority and financial support over and above the requirements of proliferation.

When Mill set out his arguments for allowing many "forms of life" he did not have in mind only the laboratory, although proliferation outside science tends to be resisted robustly – especially when it comes to alternative medicines and the spectre of frauds and charlatans putting the health of their victims at risk. However, if we allow the benefits of supporting different ideas covered above then the same applies to methodologies, with the current dominance or pre-eminence of one approach (science) no guarantee of its continuing success – or the demerits of alternatives – any more than this could be said of theories. Extending democracy to all traditions is some way off, though, even where it is agreed that self-determination should have wider application.

Proliferation is thus a principle that makes our attitude to life and learning inclusive, as well as reflexive and genuinely fallible. It is not a rule any more than parsimony is but functions to keep knowledge an open and unfinished process by never letting us stop and be satisfied with what we have.

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Selected References:

Feyerabend, P.K., Knowledge, Science and Relativism (Cambridge: Cambridge University Press, 1999).
Holton, G., Thematic Origins of Scientific Thought (Cambridge: Harvard University Press, 1988).
Mill, J.S., On Liberty (Oxford: Oxford University Press, 1991).

Thomas Kuhn: Assassin of Logical Positivism or...

Sat, 12 Jun 2010 21:03:11 +0000

By Awet Moges (2010)

In the beginning, there was nothing but
fuzzy logic, imaginary mathematics, and monolithic science.
Then the philosophy gods said, “Let Kuhn be!” And all was light.

Introduction
There are only a handful of 20th century books that impacted the world, and Thomas Kuhn’s Structure of Scientific Revolutions1 (SSR hereafter) is one of them. The SSR has had a major impact on history, sociology and the philosophy of science and changed them more than any other book in the 20th century.2 This essay will break down the book’s initial reception and analyze its subsequent evolution. At first, readers declared the SSR to have pronounced the last rites of logical positivism,3 after Quine’s Two Dogmas of Empiricism supposedly dealt a crippling blow in 1951. However, reports of the demise of logical positivism may have been premature. Recently, careful readers like Michael Friedman and Reisch found enough affinities between Kuhn’s SSR and logical positivism to declare him a post-positivist who had far more in common with major logical positivists like Rudolf Carnap. First, this essay will list the theses of logical positivism, then the counter-theses introduced in SSR, and explain why recent scholars argued that Kuhn’s ideas were less radical than they appeared, and point at parallels in Carnap’s philosophy.

About SSR
The SSR was the “application of a study of history to problems within the philosophy of science”4 where Kuhn analyzed whether theory change in science had a rational account, i.e., how and why theories replace others. Prior to SSR, philosophers explained theory change in science in a progressive manner in which better theories replace existing ones (due to parsimonious or truthlike or instrumentally successful reasons). After SSR, philosophers divided themselves in two camps: the antagonists who charged Kuhn with relativism,5 and the proponents who interpreted Kuhn as a prophet of the new philosophy of science. Both parties relied on the myth that paints Kuhn as an assassin, the giant-killer of logical positivism.

The so-called giant killer reputation has glorified Thomas Kuhn for debunking several of the main theses of logical positivism:

Reductionism – an idea or proposition can be replaced by another idea or proposition that’s simpler. For positivism, all knowledge is reducible to scientific truths.
Verificationism – the claim that the meaning of a proposition is the set of experiences that determines its truth. Thus an empirical proposition has meaning as long it has been verified or could be verified in principle. If a statement is neither analytic nor empirically verifiable, it is meaningless.
Atomism – the metaphysical claim that all reality is composed of basic and indivisible particles that’s too small to be observed by the naked eye. Russell and Wittgenstein first developed this philosophy, which in turn influenced the logical positivists.
ahistoricism – the idea that something is free or disconnected from history, or historical development. Logical positivism held scientific theories to be universal laws and law-like generalizations that are independent of history. Thus, scientific knowledge progresses linearly, and cumulatively.

In the SSR, Kuhn proposed holism, theory-ladenness of observation, incommensurability, and emphasized the historical or social view of science. Upon a first glance, it would appear they are not compatible with the theses of logical positivism.

Holism is the thesis that the whole has a philosophical and/or epistemic explanatory priority over the elements, members, or individuals that compose them. Therefore, a whole cannot be reduced to its bare essentials. Knowledge, contra positivism, cannot be reduced to scientific knowledge. For Kuhn, both theory and observation are interdependent in a holistic way, which introduces the problem of incommensurability, for choosing between competing paradigms cannot be solved by appealing to a theory-neutral factual language.

For logical positivists, scientific observation is taken to be epistemically primary, for observation provides the raw material that serves as an “epistemologically secure foundation”6 for scientific knowledge. Moreover, observation grants a shared base for theory choice. Observation as perceptual experience is neither judgmental, nor is it dependent on judgments of any kind. Because observation is independent of judgment, it is a neutral judge that can decide between rival theories.7

Kuhn argues against observation as a secure base for scientific knowledge, for it cannot decide between competing theories. The reason observation is useless is it is already affected by the very paradigm the observer works with. This leads to the notion of theory-ladenness8, which was first instituted by Norwood R. Hanson in 1951.9 Theory-ladenness is the idea that a concept or a term or a statement makes sense only in light of that particular theory. Observers do not make identical observations because what they see depends on what they know or believe.10 In other words, theory, tradition and expectations shape even experience. Every observational term already comes with theoretical baggage. If theory-ladenness is correct, then logical positivists cannot claim that a statement is a theoretically agnostic report of experience. Neither can they reduce a theory-laden term to the level of pure observation and produce a fact. If there's no theory-agnostic observational language, then how can any theory be evaluated without presupposing a paradigm? If all theories come from different paradigms then paradigms are incommensurable.

Incommensurability is the concept that theories of different paradigms are not translatable because paradigms consist of different vocabularies where neither could be fully stated in the other, or could not be translated without distortion. For logical positivists, the comparison of theories only needs the translation of their effects in a neutral observation language. According to the incommensurable thesis, there is no neutral observation language at all to mediate between paradigms.

In the SSR, Kuhn included many examples from the history of science where proponents from different paradigms failed to understand each other, and he defined this as incommensurability. For example, in physics, the Newton paradigm is not commensurable with its predecessor, the Aristotle paradigm. They lacked a common measure because their concepts and methods were different, and they focused on different problems. “..the scientist who embraces a new paradigm is like the man wearing inverted lenses.”11

“We have already seen several reasons why proponents of competing paradigms must fail to make complete contact with each other’s viewpoints. Collectively these reasons have been described as the incommensurability of the pre and post-revolutionary normal science tradition.”12

Kuhn argued that incommensurability was one reason why science does not progress cumulatively, in order to refute the notion of science as a constant moving towards an approximation to the truth. Science does not progress to a perfect ideal, but only away from the anomalies that plagues the current theory. Therefore, scientific progress is eliminative, rather than linear and instructive. 13

There is no transcendental method for rational scientific progress. Kuhn instead developed a cyclical picture of scientific progress, where a mature science operates under a paradigm, and goes through periods of normal science. Then a crisis occurs when the paradigm declines in its usefulness, falls into serious doubt, and revolutionary science results when a new paradigm replaces the old one. Finally, the revolution “inaugurates a new period of normal science.”14 Given this picture, scientific knowledge cannot be accumulative.

Normal science extends the “knowledge of those facts that the paradigm displays as particularly revealing, by increasing the extent of the match between those facts and the paradigm's predictions and by further articulation of the paradigm itself.”15 Normal science articulates the “phenomena and theories that the paradigm already supplies.”16 Kuhn characterized normal science as puzzle-solving, where results may not be spectacular but they can prove the success of a scientist. Normal science entails the existence of consensus among the community of scientists. They work on research that is based on a certain achievement they acknowledge as the foundation of its practice. 17

When this consensus breaks down during crisis, it is rebuilt during the period of a revolutionary science. A crisis takes place when anomalies multiply and scientists begin to doubt the existing core theory.18 Normal research no longer works, and some scientists realize their paradigm has ceased to function adequately and needs to be replaced. Revolutionary science is defined as a “non-cumulative developmental episode in which an older paradigm is replaced ...by an incompatible new one.”19 Conservative defenders of the old paradigm take comfort in the past achievements of the normal science, and are reluctant to give it up. They hold out hope that it will eventually survive the crisis and solve the anomalies. Radical supporters of the new theory, despite its lack of track record, recognize its future promise. Scientists from two competing paradigms are unable to understand one another since their theories are incommensurable. “..the reception of a new paradigm often necessitates a redefinition of corresponding science. Some old problems may be relegated to another science or declared entirely 'unscientific.' Others that were previously non-existent or trivial may, with a new paradigm, become the very archetypes of significant scientific achievement. The normal-scientific tradition that emerges from a scientific revolution not only incompatible but often actually incommensurable with that which has gone before.” 20A new paradigm is accepted only if it is recognized as being superior in problem solving than the competition, and the shift to the new paradigm starts a scientific revolution.

Paradigm is Kuhn's most notorious concept, for it is least precisely defined of them all. Roughly, paradigms provide the basis for normal science, and at the same time it limits the field of investigation by restricting questions and answers, and that conditions expectations. Therefore, a paradigm can affect observation, and cause the scientist to overlook anomalies, or wilfully ignore them. Kuhn defined paradigm in at least two senses: one, a global all-embracing “shared commitments of a scientific group” and the other, a “particularly important sort of commitment… a subset of the first.”21 The first definition seems to be the conscious obedience to methodology and rules, whereas the second seems to be an intuitive pattern recognition. Logical positivists would agree with the first definition, for they thought that science could be explained by the conscious obedience to methods and rules, but Kuhn's second definition denies this and proposes that exemplars serves as models for new scientists to develop their powers of pattern recognition.

Kuhn called exemplars as the “most novel and least understood aspect” of SSR in the postscript to the second edition.22 He defines exemplars as a set of recurrent and quasi-standard illustrations of various theories in their conceptual, observational and instrumental applications. These are the community's paradigms, revealed in its textbooks, lectures and laboratory exercises.23 Kuhn pointed at great works like Copernicus' De Revolutionibus and Newton's Principa as the origin of a scientific paradigm. They became paradigms because they attracted scientists and persuaded them away from other competing theories, and they were sufficiently open-ended to leave enough problems to be solved.24 Kuhn's paradigm concept helps explain the context of discovery somewhat: working with exemplars help scientists to regard new problems as puzzle-solving and allows them to potentially discover solutions to their puzzles.

One last point about positivism and Kuhn's rebellion: the foundation of the “received view” was the distinction between the discovery and justification of scientific theories.25 This distinction is essentially the distinction between psychology and epistemology, respectively. Discovery is about hunches or insights, which are psychological processes that are not beholden to conscious intention. These processes are subjective elements that come from non-rational, non-logical, and unconscious activity. Philosophers generally do not deem the context of discovery a worthwhile field of analysis, for psychologists are better suited to the task. Unsurprisingly, philosophers are far more concerned with the epistemology of scientific theories, in which they are more concerned with the reasons and arguments that support the idea. The context of justification is about rules that determine whether a hypothesis is acceptable. The problem is there are no rules that show the way to formulating the right hypothesis in the first place. Logical empiricists dismissed discoveries as irrational, for they thought discoveries were based on imaginative leaps or lucky accidents. Thus, there cannot be any logic of scientific discovery. The positivist is only concerned with “legitimizing [the discovery] scientifically, prove it objectively, and construct it logically”26

Kuhn also rejected the distinction, and at the end of the introduction to the SSR he admitted to have violated the distinction between the “context of discovery” and the “context of justification.”27 Hoyningen-Huene said Kuhn rejected the distinction because he was committed to theory choice. Kuhn considered the justification of theory choice to belong to the context of discovery because theory choice depends on the commitments of the scientific community to a paradigm. The values or norms of a community is a sociological issue, so by erasing the distinction, Kuhn shifted the issue of justification from epistemology to sociology. 28 While Kuhn’s paradigm theory did erase the distinction between truth conditions of science and its historical period, this wasn’t foreign or contradictory to logical positivism.29

Analysis of giant-killer reputation
Was Kuhn truly a giant-killer? If so, did the practice of philosophy of science truly change appreciably after Kuhn? I.e., is verificationism now bunk? Not at all. We only did away with A. J. Ayer’s formulation, for it was incoherent and exceedingly simplistic.30 Verificationism lives on today but under different names such as confirmation. Another point to note is that the initial readers of SSR exaggerated the break between Kuhn and his predecessors.31 He retained some empirical commitments which is why he only broke away from certain elements of logical positivism with concepts like incommensurability, progress, and paradigms. However, some say Kuhn failed to go far enough, for he was not radical enough. The historian Michael Friedman claimed the Kuhnian revolution was not complete and he has tried to restore Kuhn as a positivist who only forced an partial transformation in logical positivism. Had Kuhn gone far enough, he would have pulled off a truly revolutionary break with the established philosophy of science of the times.

Recent scholars have tried to rehabilitate the reputation of logical positivists with a careful attention to their work that dispelled many myths, particularly the one that Kuhn hammered the final nail in the coffin of positivism. Many scholars focused on the paragon of logical positivism, Rudolf Carnap, and found sufficient material to rehabilitate his reputation. George Reisch pointed out that Carnap's philosophy of science had much in common with Kuhn's normal science and paradigm concept. Michael Friedman rescued Carnap's philosophy from the unfair reputation of naïve empiricism and foundationalism.32 John Earman saw many affinities between Carnap and Kuhn with respect to semantic incommensurability.

In the scholars' reevaluation of Carnap’s body of work, the natural transition of logical empiricism to post-positivism diminishes Kuhn’s giant-killer status. Reisch offered the letters between Carnap and Kuhn as evidence that there was no contention between them, thus he encourages us to draw the inference that there was no incompatibility between their philosophies.

Similarities between Carnap and Kuhn are found in the Empiricism, Semantics and Ontology (ESO hereafter), where Carnap proposed the notion of linguistic framework. Some scholars33 argued that the linguistic framework could be interpreted as compatible with Kuhn's notion of paradigm, and the pragmatic nature of external questions is similar to Kuhn's value of theory choice. Carnap's linguistic framework theory is also compatible with Kuhnian theses: incommensurability, holism, and the theory-ladenness of observation. Therefore, they argue, Carnap's theory is close to Kuhn's theory of scientific revolution, normal science and paradigm.

First of all, Carnap thought that all scientific theories were embedded within a linguistic framework. Carnap was chiefly concerned with existence problems in the ESO, and in order to allow scientists to discuss abstract entities without embarrassment, he divided the problems into internal questions and external ones. For Carnap, a linguistic framework is a set of linguistic conventions that determine how we decide questions about existence. A simple example for a linguistic system would be a mathematical system with axioms, and an existence question is answered with deductions from the axioms. Carnap called this existence question an internal question. On the other hand, an external question would be about the total system of entities34, for the linguistic framework presupposes them in order to ask and answer internal questions. We can judge internal questions according to the logical rules within the individual linguistic framework, but we cannot judge external questions for they do not presuppose any logical rules.35 For Carnap, the internal questions are distinct, clear-cut and philosophically uninteresting, whereas external questions, often ontological ones, are meaningless. Thus external questions should never be asked. At most we should only be concerned whether the linguistic framework is acceptable on pragmatic grounds.

Where logical rules of a linguistic framework establish validity according to that framework, for Kuhn, a particular paradigm that regulates a normal science involves agreed-on rules that designate what counts as valid solutions for puzzle-solving problems. Where external questions, with respect to the linguistic framework under question, aren’t beholden to logical rules, but more so to pragmatic and conventional reasons, for Kuhn, a paradigm is replaced when revolutionary science changes the generally accepted rules that are in play during normal science, and requires a conversion.

Once a linguistic framework is subbed for another, a revolution occurs, for the framework is defined by its rules. Changing them will change the scientific language, and brings on a revolution. These parallels between Kuhn and Carnap inspire scholars to claim that these philosophers shared similar views about science, and how scientific revolutions take place, whether it is paradigm change or lexical change.

Objections
While it is true that there are more affinities that the “received reading” has ignored or glossed over, however, those affinities are not constitutive of a clear compatibility. This “return” to a reconciliation is but a revisionist reading, because there are several reasons, raised by J. C. Pinto de Oliveira:

It matters little that Kuhn had Carnap's support in their personal correspondence, for that hardly amounts to a clear endorsement of Kuhn's philosophy of science in the SSR.
Carnap's complete silence about Kuhn in his later work, especially in his last book, Philosophical Foundations of Physics
Carnap continued to distinguish between discovery and justification in his attempt to push a “logic of science” in the article “Logical Foundations of the Unity of Science.”
Carnap considered Kuhn's SSR a work in the history of science, not the philosophy of science, and he himself admitted that he was ignorant of the history of science.

Though Carnap claimed that the language change in his linguistic frameworks had much in common with scientific revolution, he did not go into detail about such revolutions because he thought epistemology or wissenschaftslogik had nothing to do with historical analysis. Carnap was concerned with formal problems, or how language applied to certain sciences. Whatever happened during periods of revolutionary science, he was only interested in the articulation of the logical structures of the two different languages. 36 However, history is not mere embellishment of an a priori structure of scientific rationality. Kuhn instead saw a philosophical quality in the analysis of history of science, and that is sufficient reason to refrain from lumping them together in a quasi-philosophical category.

Conclusion
Kuhn himself was a monumental paradigm in the philosophy of science, no doubt, but revisionist scholars went too far in the swinging of the pendulum against the death of the “received reading.” Their ace in the hole, Carnap's linguistic frameworks, only show superficial similarities between the later Carnap and Kuhn, and leaves the major tenets of logical positivism themselves untouched. The initial reading of Kuhn as the chief assassin of logical positivism was exceedingly simplistic, no question. But this does not excuse the equally dramatic swing to the antithetical position that tried to force Kuhn into a straitjacket that made him more germane to the descendants of logical positivism. I propose a middle solution that recognizes Kuhn may not have truly broken free from his ancestors in the philosophy of science, but his new vocabulary was sufficient in instituting a massive evolution that's still sending shock waves in the field that continues to be felt today. At any rate, scientists, like what Virgil advised Dante when it came to cranks, can only look at the philosophers squabble amongst themselves, and continue to do whatever they like.

Footnotes
1. The Arts and the Humanities claimed that the SSR was the most frequently cited book in the 20th century during the period of 1976 to 1983, and the Times Literary Supplement included it in “The Hundred Most Influential Books Since the Second World War.”
2. Alexander Bird claims the SSR was not a philosophical text, but a “theoretical history” because the book became a paradigm for the philosophy of science, which revolutionized the field with a “theoretical history of science.” (Bird, 2000, p. viii)
3. Suppes was the first to do so. This persists even today, with the Stanford Encyclopedia’s entry on Thomas Kuhn
4. Newall, Paul. Kuhn. 2008
5. Critics took issue with Kuhn for charging textbooks of science as dogma, for denying any possible objective criterion that could determine between competing paradigms, and for describing the shift to a new paradigm as a “conversion experience.” (Kuhn, 1996 p. 151)
6. Bird, 2000, p. 97
7. Bird, 2000, p. 98
8. Theory-ladenness is the basis of confirmation holism, the idea that no single theory in science can be isolated in tests for it depends on other theories.
9. In Patterns of Discovery, Hanson pointed out that observation was not as simple as the logical empiricists thought.
10. Bird, 2000 p. 99
11. Kuhn, 1996, p. 122
12. Kuhn, 1996, p. 148
13. Oberheim, Eric and Hoyningen-Huene, Paul. “The Incommensurability of Scientific Theories.” 2009
14. Bird, 2000 p. 25
15. Kuhn, 1996, p. 24
16. Ibid
17. Kuhn, 1996, p. 10
18. Bird, 2000 p. 43
19. Kuhn, 1996, p. 92
20. Kuhn, 1996, p. 103
21. Kuhn, The Essential Tension, p. 294
22. Kuhn, 1996, p. 187
23. Ibid, p. 43
24. Kuhn, 1996, p. 10
25. Hans Reichenbach introduced this distinction in 1938 in Experience and Prediction where he noted the concept of rational reconstruction was essentially about how they communicate thoughts, rather than how they are subjectively formed.
26. Fleck, 1979, p. 22 Ludwik Fleck argued that the distinction between justification and discovery was exceedingly shallow, for the historical process of discovery mattered a great deal for epistemology. Fleck proposed a “thought-collective” and defined it as “a community of persons mutually exchanging ideas.” In order to discuss or exchange ideas, two people must possess the same vocabulary, and share many things in common – theories, facts, significance – i.e., beliefs and dispositions. Thus, the total knowledge of a community cannot be reduced to its individual members.
27. Kuhn, 1996, p. 8
28. Hoyningen-Huene, Paul. 2006 p. 127
29. Otto Neurath compared science to at boat we are rebuilding while at sea. A caricature of logical positivism would use the skyscraper edifice instead to represent their conception of science.
30. Alonzo Church and Carl Hempel also contributed to the decline of verificationism. Church heavily criticized the concept of verificationism in his review of Ayer's book Language, Truth and Logic in Journal of Symbolic Logic.
31. It’s interesting to note that Kuhn, despite his giant-killer reputation, did not make many references to Logical Positivists in the SSR. Alexander Bird points out that in the 150 footnotes, only 13 were philosophers. The rest consisted of historians. (Bird, 2000 p. x)
32. In Reconsidering Logical Positivism, Friedman argues that Carnap's Der logische Aufbau der Welt was not a program of naïve empiricism but instead a neo-kantian project that was concerned with the conditions for possible knowledge.
33. Reisch, 1994, and Earman, 1993
34. or the system of math, entities would be about numbers in general.
35. Carnap writes that only philosophers raise external questions, especially questions about the reality of the world.
36. Carnap, 1934, §72 “Philosophy replaced by Logic of Science”

Bibliography

Bird, Alexander. Thomas Kuhn Princeton University Press. Princeton, NJ. 2000

Carnap, Rudolf. Logische Syntax der Sprache. 1934 (English Translation) The Logical Syntax of Language. London: Routledge. 1937

Carnap, Rudolf. “Logical Foundations of the Unity of Science.” in International Encyclopedia of Unified Science. Vol. 1, no. 1. Chicago. Chicago University Press. 1938

Carnap, Rudolf. “Empiricism, Semantics, and Ontology.” in Meaning and Necessity: A Study in Semantics and Modal Logic. University of Chicago Press. 1956

Church, Alonzo. “Review of Ayer's Language, Truth and Logic.” Journal of Symbolic Logic. Vol. 14. 1949. p. 52-53.

Earman, John. “Carnap, Kuhn, and the Philosophy of Scientific Methodology.” in World Changes. Horwich, P. (ed.) MIT Press. Cambridge, Massachusetts. 1993 p. 9 – 36

Fleck, Ludwik. Genesis and Development of a Scientific Fact. Trenn, T. J. and Merton, R. K. (eds), F. Bradley (trans.), foreword by T. S. Kuhn. Chicago: University of Chicago Press. 1981. [Translation of Fleck 1935]

Friedman, Michael. “The reevaluation of Logical Positivism.” Journal of Philosophy, Vol. 88, 1991. pp. 505 – 523.

Friedman, Michael, Reconsidering Logical Positivism. Cambridge, UK. Cambridge University Press. 1999.

Hanson, N. R. Patterns of Discovery. Cambridge. Cambridge University. 1958.

Hoyningen-Huene, Paul. “Context of Discovery versus Context of Justification and Thomas Kuhn.” in Revisiting discovery and justification. ed. Schickore, Jutta and Steinle, Friedrich 2006.

Irzik, Gurol and Grunberg, Teo. “Carnap and Kuhn: Arch Enemies or Close Allies?” The British Journal for the Philosophy of Science. Vol. 46, No. 3 September 1995. pp. 285 – 307

Kuhn, Thomas. The Essential Tension. Selected Studies in Scientific Tradition and Change. Chicago: University of Chicago Press. 1977

Kuhn, Thomas. The Structure of Scientific Revolutions. Chicago. University of Chicago Press. 1996

Newall, Paul. “Kuhn.” 2008 The Galilean Library.

Oberheim, Eric and Hoyningen-Huene, Paul. “The Incommensurability of Scientific Theories.” 2009 Stanford Encyclopedia of Philosophy. Stanford University. 25 February 2009

Oliveira, J. C. Pinto de. “Carnap, Kuhn, and revisionism: on the publication of Structure in Encyclopedia.” (4th version) 2007 Springer Science + Business Media B. V. 6 June 2007 (online)

Reisch, George. “Did Kuhn Kill Logical Empiricism?” Philosophy of Science. 58 (2). 1991 p. 264 – 277.

Reisch, George. “Planning Science: Otto Neurath and the International Encyclopedia of Unified Science.” British Journal for History of Science. 27 1994. p. 153 - 75

Reisch, George. How the Cold War Transformed Philosophy of Science : To the Icy Slopes of Logic. New York: Cambridge University Press, 2005.

Anything Goes: Feyerabend and Method

Sat, 12 Jun 2010 19:51:12 +0000

By Paul Newall (2005)

Perhaps one of the least understood arguments in the philosophy of science, Paul Feyerabend's reductio ad absurdum of specific rationalist conceptions of scientific method is at once a subtle critique of rigidity in thinking and an historical study of Galileo's rhetorical strategies in the latter’s discussions of Copernicanism. In this paper we explain the structure of the reductio before considering how Feyerabend applied it.

When Feyerabend first published his Against Method, he was explicit concerning his aim:

Quote

My intention is not to replace one set of general rules by another such set: my intention is, rather, to convince the reader that all methodologies, even the most obvious ones, have their limits. The best way to show this is to demonstrate the limits and even the irrationality of some rules which she, or he, is likely to regard as basic. (1975, 32)

He went on to entreat the reader to "always remember that the demonstrations and the rhetorics used do not express any 'deep convictions'" of his. Nevertheless, this work has consistently been described as an attempt to advance and defend the methodological principle "anything goes", so much so that Munevar complained that "it should be an embarrassment to the profession that many reviews were completely unable to see the structure of this simple reductio" (1991, 181). (See Laudan, 1996, for an excellent example of a total misunderstanding that borders on the ridiculous, as well as Newton-Smith, 1981.) As a measure of his exasperation at such empty critiques, Feyerabend’s Science in a Free Society contains an appendix entitled "Conversations with Illiterates" (1975, 125-218), in which he responded to some of his detractors.

In general, a reductio ad absurdum is a form of argument in which the proponent may take as given the premises of the opponent while explaining how their acceptance leads to absurd consequences. As a result, one or more premises must be rejected. (This is widely used in mathematics.) The structure of Feyerabend’s reductio is quite straightforward, notwithstanding its confusion with a positive argument for anarchism: faced with the methodological principles of certain forms of rationalism (or what Feyerabend thought of under this rubric, most notably logical positivism and falsificationism) and so-called paradigmatic instances of these at work in the history of science, Feyerabend sought to show that the same rationalists would have to admit that science has developed in a fashion either contrary to their standards or otherwise in a manner that they would have to characterise as irrational.

As a result of this rhetorical strategy, Feyerabend was able to explain himself clearly:

Quote

'Anything goes' is not the one and only 'principle' of a new methodology, recommended by me. It is the only way in which those firmly committed to universal standards and wishing to understand history in their terms can describe my account of traditions and research practices ... If this account is correct then all a rationalist can say about science (and about any other interesting activity) is: anything goes.

The reductio thus took the following form:

Take the principles of a rationalist methodology for science;
Consider what the same rationalists propose as a representative example of such a methodology at work in the history of science;
Note that the decisions made on the basis of a rational methodology should, ceteris paribus, be rational; and
Demonstrate that an account of this episode in such terms forces us to describe the actions of those purportedly following the rules as irrational or in violation of them.

Before we look at Feyerabend's argument, it is useful to take a simple example of a reductio at work. If we subscribe to the tenets of dogmatic falsificationism (or else advocate basing our acceptance and rejection of scientific theories on so-called decisive experiments) and suppose Einstein's Special Theory of Relativity to have been a step in the right direction with regard to gaining knowledge of our universe, we find that we run into a problem. Falsificationists do not dispute the historical account of 1905, in which the first response to Einstein's paper noted that his theory had already been refuted by Kaufman's experimental results, published in the Annalen der Physik in that year. The dogmatic falsificationist is thus forced to admit that Einstein should have dismissed his theory as falsified – which, of course, he did not. We are led to the unfortunate position of either arguing that Einstein was irrational (or mistaken, if we wish to be more charitable) in his refusal to give up the special theory (and moreover that we, as good falsificationists, would have rejected it, along with any consequences) – a demand we would probably call absurd – or else accepting that dogmatic falsificationism fails.

Feyerabend preferred to use another – more famous – example from the history of science: Galileo's work on geostaticism. His reductio consisted in three stages, designed to critique na�ve empiricism, Popper's falsificationism and Lakatos' Methodology of Scientific Research Programmes in turn – each being an instance of a rationalist approach to science (in the case of the latter two, the most common even today). For the first of these, he considered the famous Tower Argument, a circumstance relied upon by Aristotelians to discount the possibility of a moving Earth. Its proponents pointed to the fact that a stone dropped from a tower lands at its base. If the Earth was moving, as some supposed, the tower would move with it and hence the stone would drop some distance away. (A variant of the same argument stated that an arrow fired vertically into the air should fall far from the firer, since he or she would have moved along with the earth while the arrow was in flight.) This was an idea everyone could understand and hence served as a powerful refutation of the notion that the Earth moves.

It matters not at this stage whether Galileo was an empiricist or not: in order to undertake a reductio, we assume that he was and see what follows. What Galileo did was to accept the observations made by those who had tested this theory (that the stone falls at the base) and then appeal to a principle of relativity (often called Galilean relativity). He asked his readers to imagine two friends throwing a ball to each other while inside a cabin on a ship alongside and then the same situation while the ship was underway, considering whether more (or less) force would be required to throw the ball when the ship was moving. This was also a test that most people could understand and it helped him to explain that there was no difference because any motion of the ship would also be shared by the passengers. That is, whichever direction the ship moved in, the cabin would, too - along with everything inside it.

As a result of this discussion, Galileo was able to demonstrate that the very same "fact" used by the Tower Argument itself - the stone falling at the base - also supported the idea that the Earth was rotating, since any evidence that the geostaticist could appeal to would likewise support the alternative (this is actually an example of underdetermination by data and the theory-ladenness of observational terms). The naive empiricist has no means of deciding between these two rival theories and hence any choice made by Galileo would violate this form of empiricism. If our methodology insists that only those decisions made on the basis of evidence can be called rational then Galileo and the Aristotelians alike were irrational to prefer geokineticism or geostaticism respectively. We are thus forced either to give up on calling Galileo's behaviour rational or else admit that naive empiricism is inadequate.

The reductio of Popper's falsificationism proceeded in a similar way. Copernicus' system predicted magnitudes for both Venus and Mars that were refuted by observations, which led to the same conclusion with regard to dogmatic falsificationism as in the example of Einstein above. Feyerabend considered the sophisticated version of falsificationism, though, according to which Copernicanism should have excess empirical content over the Ptolemaic model, including the prediction of novel facts that were falsifiable. Unfortunately, Copernicanism was of equal empirical content to its rival (see Kuhn, 1985 and Swerdlow, 1973) and was incompatible with the Aristotelianism of the day. This latter point is an important one to appreciate: Aristotelianism did not merely consist in an astronomical theory concerning the heavens but was an integrated system that applied widely. In particular, Aristotle’s dynamics was a theory of change, including explanations of generation, corruption, locomotion and qualitative change. The dynamics that Galileo proposed in its stead dealt only with locomotion, which was a decrease in truth-content (as always, from the perspective of that time). Thus we find that Copernicanism represented a theory that was falsified, of equal empirical content and of lesser-truth content. As Popperian falsificationists, we are forced again to admit that Galileo was irrational to persist in his studies or that Popper's methodology is flawed.

The last reductio that Feyerabend attempted – that of Lakatos' much more subtle approach – could not rely on his analysis of Galileo’s behaviour, since Lakatos was in complete agreement (Lakatos and Zahar, 1975; see also Lakatos, 1978). Since Lakatos' methodology was careful to incorporate the lessons of the failure of falsificationism, his classification of research programmes as progressive if they demonstrate excess empirical content that has been confirmed (and degenerating for the converse) was far better equipped to survive problematic episodes in the history of science. Indeed, Lakatos accepted that a new theory would initially show a loss in empirical content as it took time to become established, and that ad hoc measures are acceptable insofar as they help the theory avoid falsification and thus give it more time to develop. The obvious difficulty with such a methodology, of course, is where to draw the line at all when so much wriggling is permitted; after all, a degenerating theory could eventually become progressive again if given the opportunity (or even if not). This is where Feyerabend addressed his argument.

Introducing the concept of an epistemological anarchist, this being a person with an aversion to ideologies and opposing "positively and absolutely" all universal standards (1975, 175), Feyerabend asked how the actions of an epistemological anarchist at the time of Galileo would differ from those of a Lakatosian. It was immediately clear that the former could do as he or she liked, by definition, but what of the Lakatosian? Herein lies the problem: Lakatos' Methodology enables us to describe a situation but it does not tell us how we should act. A Lakatosian could accept Aristotelianism as a progressive research programme and reject Copernicanism as degenerating, but he or she could also do the converse. No restriction is placed on what should be done; all we have is a new vocabulary to explain ourselves.

The reductio in this last case thus consisted in referring again to the "methodology" of epistemological anarchism – or the "anything goes" we began with – and showing that Lakatos' approach could not be distinguished from it. Since "anything goes" is no method at all, rendering everything rational at a stroke, it followed that either we should follow a method that is not a method (which is absurd) or else reject the Methodology of Scientific Research Programmes.

The glaring point to notice in each of these arguments is that nowhere is it necessary for us to accept that there is no possible scientific method; that "anything goes"; that we should all become epistemological anarchists; or that Feyerabend was advocating any of these. All these terms and concepts, employed in critiques of Feyerabend then and since, are intended for use inside the context of a reductio ad absurdum only. The subtlety of this form of rhetoric (which Galileo himself had mastered) is lost when we interpret it as an attempt to replace one set of rules with another (in the face of Feyerabend's own declaiming the possibility), leaving us with mere caricatures and an understanding of the philosophy of science so much the poorer.

---

Suggested references:

Feyerabend, P., Against Method (London: Verso, 1975)
Feyerabend, P., Science in a Free Society (London: New Left Books, 1978)
Kuhn, T.S., The Copernican Revolution (Cambridge, Mass: Harvard University Press, 1985)
Lakatos, I., The Methodology of Scientific Research Programmes (Cambridge: Cambridge University Press, 1978)
Lakatos, I. and Zahar, E., Why did Copernicus' Research Program Supersede Ptolemy's?, in Westman (ed), The Copernican Achievement (Berkeley: University of California Press, 1975)
Laudan, L., Beyond Positivism and Relativism (Boulder: Westview Press, 1996)
Newton-Smith, W.H., The Rationality of Science (Boston: Routledge and Kegan Paul, 1981)
Swerdlow, N., The derivation and first draft of Copernicus's planetary theory: a translation of the Commentariolus with commentary (Proceedings of the American Philosophical Society, 1973, 117: 423-512)

Lakatos and the Demarcation Problem

Sat, 12 Jun 2010 19:47:16 +0000

By Paul Newall (2005)

According to lore, Imre Lakatos was an excellent speaker and a highly amusing one. (He would often listen in on Paul Feyerabend's talks from his office and shout rejoinders if the latter got too carried away.) He wrote a series of lectures on scientific method that were collected in Motterlini's For and Against Method, which we consider here as a means of discussing demarcation in science. It covers some of the discussion in his public talk Science and Pseudoscience

The first lecture dealt with the Demarcation Problem, which Lakatos rendered as "what distinguishes science from pseudoscience?" He then provided four examples of why it is important (and "not an esoteric problem for just armchair philosophers"): the historical debates over Copernicanism; the Lysenko affair in the Soviet Union; the studies done concerning the link, if any, between IQ and race; and finally Velikovsky's ideas. We could add another that most of us are familiar with: the question of creationism in schools, in which it is said that creationism should not be allowed in the science classroom because it is not scientific at all but rather pseudoscience. To make this sort of claim, however, requires – implicitly or otherwise – a demarcation criterion (or criteria) that allows us to specify what is or is not science.

Lakatos remarked – casually, as it were – that Karl Popper was once a cabinet maker, helping us to imagine Sir Karl constructing a special example of his craft into which we would feed theories and have the thing tell us if they are meaningful or not - a "sausage machine", as it were, heaping theories into piles marked "science" and "pseudoscience". This was not just a subtle dig for the amusement of his students: the demarcation problem can be viewed in this way to make it clearer what the issue is. Given a theory, what formula do we have to run it through before we can say "this is a scientific theory" and (provisionally) accept it as interesting or "this is pseudoscience" and (presumably) dismiss it? Lakatos contrasted Hegel's ideas – those we would now consider obviously pseudoscientific and hence a straightforward example – with Velikovsky's, whose case was not so simple. According to Popper's falsificationism, for instance, Velikovsky’s theories were scientific; and yet they were rejected by most astronomers. Later Lakatos came back to problems with falsification and why we need more, but at this point he hinted that demarcation in the natural sciences would be much easier than in the social sciences. His joking example of burning down the London School of Economics (LSE) shows again how important the demarcation problem is in general: when politicians decide to invade another country, say, they have – like it or not – used a demarcation criterion (or criteria) to decide where the line was and when it was crossed such that they had to act.

Lakatos went on to explain some of the positions historically taken on the demarcation problem. The militant positivists believed (and still believe) both that we can find demarcation criteria and that we ought to divide up theories into good or bad accordingly. We also have skepticism, to which Lakatos gave other names. This was a (likely deliberate) straw man, but we come back to it later and consider whether it was a fair description of what sceptics like Feyerabend actually said (as well as if there is such a thing as epistemological anarchism). He then spoke of intellectual honesty, or whether it is acceptable morally to propose pseudoscientific theories or try to convince others of them. (For Popper it was - and many commentators today still is - wrong to advocate pseudoscience, however well-intentioned we might be in doing so.)

Returning to demarcation criteria, Lakatos then talked about elitist authoritarianism (which is somewhat similar to Dickie’s Institutional Theory in the philosophy of art): what is or is not science is demarcated by scientists (just as what is or is not art is decided by artists and museum directors, according to Dickie). This is a method of demarcation (favoured by Polanyi) but does not give - or rely upon - demarcation criteria at all. He gave some justification for this position before bringing it crashing down with two questions:

How do scientists (or philosophers, or whomever) come to disagree with one another?
How do scientific revolutions come about?

In the first instance, it often happens that some scientists hold to one theory while others support another (or even still others). If all the scientists concerned are "good" scientists (whatever that means), how do we decide which theory is scientific and which pseudoscientific? Elitist authoritarianism appears to give us no guidance. For the second, Lakatos gave a brief (and - it must be said - dismissive) introduction to Kuhn and asked an important question for all forms of demarcation criteria: how do we get started in science? That is, suppose we begin over and ask how we decide which theories are scientific and which pseudoscientific. There are no scientists to help us decide, after all. What can be done?

In his second lecture, Lakatos began by saying a few words about positivism and Popper's determined opposition to it. (The amusing subscripts he used were (as the footnote says) thrown right back at him by Feyerabend later.) Hopefully it is at least clear on reading that Lakatos had a wicked (yet subtle) sense of humour, which he employed often. This was likely one of the qualities that brought about his friendship with Feyerabend. Lakatos explained that he would set out the various possible answers that have been given to the demarcation problem. If we find that they all fail, he said, we have to accept Feyerabend's or Polanyi's alternative. We need not concern ourselves with whether Lakatos was giving a falsely limited choice here (i.e. other suggestions could come along at a later date or the problem itself might need redefining or dispensing with altogether), reading it instead as accompanied by much winking at his audience.

Talking a little about the so-called Dark Ages, Lakatos noted that in the seventeenth century the standard used for science was a form of justificationism, according to which knowledge is justified by reference to fixed standards. These standards could be experience, holy texts, or even - said Lakatos - the balance of probabilities. He then remarked: "So it is quite clear that these standards have theological origins."

The idea here is that - in the past - appeal was made to scripture to justify a statement because to utter a false comment on a religious matter could lead to damnation. Some, like Popper (in Lakatos' opinion), believed or believe something very similar about scientific theories - that it is wrong to publish or hold to a pseudoscientific theory. Lest this seem overly dramatic, we can refer back to the examples in the discussion of the first lecture and see that perhaps it is not. In particular, we need only consider the reactions on the part of some members of the scientific community to advocacy of Intelligent Design, so-called, to see a fervour in opposition that could easily be described as "religious" and the envy of many a pious churchman of the Middles Ages.

Lakatos then talked about inductivism, pointing out that to justify a theory by reference to facts we require two important steps:

Quote

(1) from a fact to a factual proposition describing the occurrence; and (2) from a factual proposition which is spatio-temporally singular to a spatio-temporally universal proposition.

This is, of course, the celebrated problem of induction. Note, however, that Lakatos was distinguishing two difficulties, while we usually only talk about the second. To use his example, the steps are:

Quote

(1) - from "chalk exists", "blackboards exist", "I exist", and so on, to "this is a piece of chalk and it writes on the blackboard"; and
(2) - from "this is a piece of chalk and it writes on the blackboard" to "all pieces of chalk write on the blackboard".

Can these be bridged? Apparently not, since inductive inferences have long be known to be invalid. (Mill's 1843 [2002] system of logic, however, is considered by some to be the best approach to the problem of induction.) The second step is what we usually think of as the inductive inference involved in science, but the first is necessary also. Lakatos concluded that inductivism (or justificationism) will not suffice as a demarcation criterion and hence should be rejected, a position accepted by all.

Lakatos began lecture three by expanding on his previous remarks about the unbridgeable steps from facts to factual propositions and from the latter to inductive justifications. He then went on to discuss theory formulation, first considering the idea (inductivist and still quite common) that we observe the facts and use them to build theories. In the case of planetary hypotheses, he said, people instead were already sure that planets had to move in circles (due to Aristotle's ideas, and others) and looked for evidence to justify it. This is interesting because it tells us something about the way science proceeds: according to the inductivist, science starts with facts and induces theories from them, but this example from the history of science shows that actually astronomers were convinced already (for mathematical, philosophical and other reasons) that planets move in circles and used their observations to justify this. Another section on the myth that Einstein's theory of special relativity was derived from the famous Michelson-Morley experiment is tackled in more detail by Holton. This is part of a general discussion (Lakatos' other main instance was the notion that Newton's laws were derived from Kepler's) of inductivism giving birth to historical yarns that have little or no foundation. When we note in this way that famous instances of scientific work fail to match the methodology we insist science follows, we either have to give up the methodology or stop calling the work scientific.

The notion that the probability of a theory is always zero was, as Lakatos noted, derived by Popper and included as an appendix in his The Logic of Scientific Discovery. (A look at the interpretations of probability - emphasing the difficulties - is here. It is important to understand that Lakatos was treating of the assignment of probabilities to scientific theories on the basis of the available evidence, not confidence intervals.) The idea, in brief, is that there are infinitely many theories that may account for the available data set (this is the problem of underdetermination, of course). Following Goodman (1983), a nice way to appreciate the difficulty is to suppose that the data are points on graph paper and then ask how many lines may be drawn between all of them. The answer, trivially, is an infinite number. It would follow that the probability of any one being correct is zero.

It seems the misunderstanding arises when confusing a theory with an hypothesis. A confidence interval is used to accept or reject a null hypothesis, not a theory. Perhaps Lakatos was guilty of being careless with this distinction? For instance, he says that a "scientific hypothesis says..." and immediately follows his example by remarking that the "information content of such a theory..." The inverse squared law of gravitational attraction (his example) is clearly a law. The possession of a characteristic, on the other hand, is neither a law nor a counter-example. A finite (although large) number of confirming instances makes no difference - a single counterinstance will disprove the hypothesis. The accumulation of confirming observations runs smack into the problem of induction, since the prior results do not make the next any more likely to possess the desired characteristic unless we assume it to be law-like in the first place - thereby begging the question. (See the discussion of confirmation.) As Lakatos also said, however, there have been attempts to develop an inductive logic - by Tarski and more recently by Hintikka and others (see Lakatos, 1968).

In his fourth lecture, Lakatos used the discussion of verificationism to get in a few choice jibes at the positivists' expense. Beginning with Schlick's version, he explained that it was quickly shown to be untenable because inductive inferences (particularly laws) cannot be meaningful under such a demarcation criterion (that is, to verify a statement like "all swans are white" – the example he used – we would need to see all swans and verify their whiteness individually). A healthy disdain then followed for Ayer's ([1936] 1946) attempts to rescue verificationism, noting that those propositions that the positivists wanted to exclude (like religious or ethical ones) could be made meaningful under Ayer's terms. This was a reductio argument.

In the next look at "super direct" verificationism, Lakatos' humour came again to the fore:

Quote

In 1492, however, Columbus had discovered America, and that led to some trouble because in 1949 an American named Alonzo Church reviewed Ayer's book...

Here Lakatos was alluding to Church's proof (1949) that all statements would be verifiable, the reaction to which was, according to Lakatos, an increasing "scholasticism", eventually culminating in a nine-page definition of verification including logical conditions that would have to be satisfied. Although Lakatos had some fun with this, his point was clear: such criteria are no use at all to scientists or anyone else trying to sort theories into good and bad (or deciding which books to burn, alluding to Hume’s famous declaration).

Moving on to conventionalism, Lakatos discussed in a lengthy aside the rise of instrumentalism via the Ptolemaic astronomical system. Here we see a rare instance of error: contrary to the claims of some philosophers of science, Ptolemy did not accept that his theory was only a tool and instead tried to develop a realistic understanding of it - nor, for that matter, did Copernicus "get in trouble" simply because his theory apparently contradicted certain Scriptural passages (instead his theory was unconvincing for reasons that are explained in the essay on Galileo). In any case, and in spite of Lakatos' mistakes, the point of conventionalism is to use theories as instruments and not worry about whether they are true or not in reality - we call them true by convention.

This explanation was followed by still more stories, including the realisation in the nineteenth century that any convention could be saved by enough ad hoc hypotheses, so that conventionalism fails to demarcate at all. (This does not address the question raised in Lecture two, however, by pointing to the demise of instrumental theories.) Moreover, the problem for conventionalism is what to do with established theories. Since these are accepted by convention, we seem drawn into the conclusion that experiment can refute a new theory but not an old one - that is, the power (and relevance) of empirical investigation seems to lessen the more science develops and expands. Unfortunately the fifth lecture - entitled The Limits of Conventionalism - was lost, in which Lakatos expanded on this matter.

In lecture six, Lakatos began his critque of Popper's falsificationism by reiterating that the demarcation problem has typically involved a moral claim; namely, that it is wrong (or irresponsible) to insist upon a theory that is unproven; and since ideas have consequences, we should be careful when speculating. (Sadly Lakatos followed Feyerabend (1987) here by accusing Galileo of not following this advice, saying that "Galileo's crime was to propound Copernicus's system not as a calculating device, but as the truth about the universe." It is explained elsewhere why this interpretation is mistaken.)

For Popper, there was a failure of intellectual honesty in advocating unfalsifiable propositions. By considering Bohr's theory of the atom at length (and in some depth), alongside his own experiences in Hungary, Lakatos showed how difficult it would be to force the historical process that led to Bohr's theory into the straightjacket of falsificationism. Remarking on another example, Lakatos pointed out that Newton's laws were falsified by the discovery in 1816 of the anomalous perihelion of Mercury; and yet the laws were maintained until the discrepancy could be accounted for in 1916 by Einstein's theory of gravitation. This makes for a century of moral failure on the part of those who refused (or neglected) to do their duty and give up a falsified idea. Such stories are part of the historical approach in the philosophy of science. By demonstrating an inconsitency between a philosophical account of what science is supposed to be and how scientists actually behave, we are forced to admit either that scientists behaved irrationally or to give up the account.

In the last lecture, Lakatos continued his demolition of Popper by again referring to some of the issues discussed in our look at falsificationism, specifically the question of ceteris paribus clauses:

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... suppose we take Newton's three laws of dynamics, plus the law of gravitation, plus twenty-seven initial conditions, plus thirty-seven observational theories, and we derive an observational statement which is inconsistent with all this, what should we do? Should we cross it all out?

We learn that Popper's interest in the demarcation problem grew from a frustration in talking about politics and/or psychoanalysis in his early student years with people who always seemed to be able to find a way out of any difficulty he could bring up, which led to an interest in theories being decidable. What Popper tried to develop thereafter was a demarcation criterion that would call Newton's or Bohr's theories scientific but not Marx's or Adler's. Lakatos was able to show via examples such as those already detailed above that the insistence on falsification would render all theories unscientific. Popper tried to avoid this - desperately, at times - by implicitly claiming for himself the right to decide whether an anomaly is serious or not, even insisting in a television interview that Mercury's perihelion was not. What we see, then, is that Popper's falsificationism degenerates into a version of authoritarian conventionalism, since he could not avoid relying on the judgement of scientists (or, more often, his own...) as to when we should consider a falsifier strong enough to bring to bear all the weight of moral authority in demanding the theory's rejection and when to "wait and see" instead.

In closing this section, Lakatos remarked as follows:

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I think that the fact Popper's philosophy survived for so long is a sociological mystery. Popper's immortality is secured by this idiotic result.

Lakatos was writing in 1973. Even today, however, Popper's name is spoken with reverance and his falsificationism appealed to as either the definitive statement on what characterises science ("a theory should be falsifiable if it is to be considered scientific") or an important part thereof. The same moral indignation at refusing to dispense with unfalsifiable ideas can be found wherever science is discussed in vaguely philosophical terms. The strange thing is that - however harsh Lakatos' words may seem - the high regard for falsificationism in one form or another persists in spite of philosophers of science have thoroughly destroyed it as a credible demarcation criterion. The commitment to it is perhaps explained by the political and rhetorical importance of demarcation in the public sphere.

Given the failure of so many demarcation criteria, is this really a problem at all? There are two main reasons why it is: firstly, we do demarcate (especially given that time and resources are finite, leading to the question "how long is long enough?"); and secondly, this demarcation has consequences. A budding theory on the right end of a demarcation can potentially benefit from funding, further research and the support of the so-called scientific community; while conversely a declaredly pseudoscientific idea can be mocked, vilified in the (scientific and general) press and be unlikely to improve its station due to a lack of financial backing (although this does not always hold), while the layman or - worse - scientist responsible can expect personal and professional attacks. This latter phenomenon, indeed, is the modern-day equivalent of the Popperian moral revulsion at advocating pseudoscience - considered by many to be dishonest at best, if not the very definition of "anti-scientific" behaviour.

There can be little doubt that demarcation criteria still play an important role in science, finding their way into the debate over climate change and with critiques of creationism and intelligent design repeatedly calling on a form of falsificationism (usually the most simplistic). An increasing number of studies are showing the way in which rhetoric shapes science, too, and particularly the importance of rhetorical dimensions in achieving demarcation (especially implicit or explicit claims of authority). When we take the time to examine these controversies, we find that the philosophical failure of demarcation criteria does not prevent them being employed, even if this may backfire or encourage an uncritical tone throughout. As usual, the possibility of genuine dialogue is the victim.

What we learn from Lakatos' lectures is that the demarcation problem is alive and well, even if the most frequent usages of demarcation are na�ve and propagate long-dead myths of their efficacy in distinguishing between science and pseudoscience. The importance of going over these failures, however, lies in Mill's principle that a truth unrehearsed and unchallenged becomes a dogma far too easily. That it is so difficult to define what science is shows us not a failing but the very strength of this mode of inquiry in the first place.

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Selected References:

Ayer, A.J., Language, Truth and Logic (London: Gollancz, 1946).
Church, A., Review of Ayer, Language, Truth and Logic in Journal of Symbolic Logic, 14(1), pp52-53, 1949.
Feyerabend, P.K., Farewell to Reason (London: Verso, 1987).
Goodman, N., Fact, Fiction and Forecast (Cambridge, MA: Harvard University Press, 1983).
Lakatos, I., The methodology of scientific research programmes (Cambridge: Cambridge University Press, 1978).
Lakatos, I., The Problem of Inductive Logic (Amsterdam: North-Holland Publishing Company, 1968).
Mill, J.S., A System of Logic (Honolulu: University Press of the Pacific, 2002).
Popper, K.R., The Logic of Scientific Discovery (New York: Basic Books, 1959).

Underdetermination

Sat, 12 Jun 2010 19:39:02 +0000

By Paul Newall (2005)

A familiar sight in the philosophy of science is reference to the underdetermination of theories by the available evidence. In this short paper we will explore some examples of this phenomenon and the reasons why it is posited as a problem.

In 1543, Nicholas Copernicus published his De revolutionibus orbium celestium and, in the years that followed, some philosophers and astronomers took up the idea of a Sun-centred universe with a moving Earth. However, when Cardinal Bellarmine had occasion to write to Foscarini about whether or not Galileo and others had been able to demonstrate the truth of heliocentrism, he suggested that

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... it seems to me that Your Reverence and Galileo did prudently to content yourself with speaking, and not absolutely, as I have always believed that Copernicus spoke. For to say that, assuming the earth moves and the sun stands still, all the appearances are saved better than with eccentrics and epicycles, is to speak well; there is no danger in this, and it is sufficient for mathematicians.

He was discussing the notion that the Copernican system was able to save the appearances; that is, that it was possible to explain what was observed in the heavens on the basis of Copernicus’ theory. Although Bellarmine allowed that this theory could be considered better than the "eccentrics and epicycles" of the Ptolemaic/Aristotelian system, in fact it employed approximately the same number of these devices. Although Galileo was able to point to his telescopic work, this was unable to provide the demonstration he sought. The judgement of the day, then, was that it was impossible to choose between the Copernican and the Ptolemaic/Aristotelian systems on an empirical basis; and this is an assessment that philosophers and historians of science agree on today.

We call this situation underdetermination: the available data do not permit us to make a decision between two (or more) rival theories. Although some thinkers have suggested that this is only a minor problem, since it occurs only rarely, this is not the case. In particular, if we consider gravitational theories or the situation in contemporary physics since the advent of quantum theory, this position is untenable. Nevertheless, it is important to clarify the difficulty: underdetermination is found when we compare two large-scale theories, not isolated ones. This is because when we talk about a "theory", we do not mean (and cannot mean) a singleton, considered on its own. Following an argument from Quine, our theories are always interconnected, mutually supporting one another. In particular, any theory needs a host of auxiliary hypotheses in order for us to use it, which forms a criticism of methodological falsificationism.

Given that sometimes theories are undetermined, then, how can we decide between them? An obvious answer, of course, is not to decide at all. If we cannot find a way to make a demarcation then we could simply take an agnostic position and admit we do not know which is "better". In that case, we could divide our efforts between the two (or more) and see if there is subsequently a difference that comes to light as they are developed further. The is sometimes called methodological pluralism or the proliferation of theories.

A second response is to realise that empiricism does not hold the status once ascribed to it: we do not accept or reject theories based solely on the evidence for them but also on account of many non-empirical criteria, such as parsimony; internal consistency; beauty (for example, Copernicus’ certainty that a Sun-centred system was more aesthetically appealing); explanation; the ability to make novel predictions; and so on. This does not answer underdetermination so much as accept it as a limitation on empiricism, which can thus only take us so far in the matter of theory evaluation and choice.

Strong Underdetermination

The recognition that evidence is not the only heuristic we employ in deciding between theories allows us to distinguish between two forms of underdetermination: strong and weak. The first of these tells us that there is no way to distinguish between theories with the same observable consequences – called empirical equivalence – and points to the existence of an infinity of possible theories consistent with any finite data set. For example, the theories "general relativity" and "general relativity plus 'New Zealand will win the next Rugby World Cup'" are equally supported, but their comparison seems absurd.

Indeed, strong underdetermination is typically rejected because it fails to note that we do not claim to be able to choose between empirically equivalent theories on the basis of empirical criteria, which is impossible by definition. Moreover, it relies on an implicit separation of theory and observation: when we say that the evidence underdetermines the theory choice, we run up against theory-ladenness. Since we cannot distinguish between theory and observation in a straightforward fashion, we cannot appeal to or rely on theory-neutral observations and say that these disallow the possibility of making a choice. After all, the observations that give us this problem of underdetermination in the first place are themselves theory-laden. In brief, then, we cannot say that underdetermination makes theory choice impossible because we already use theory in obtaining the evidence that leads to underdetermined theories to begin with.

The combination of this limitation and untenable theory/observation distinction makes strong underdetermination too bold a claim.

Weak Underdetermination

The second form of underdetermination acknowledges these difficulties but makes a weaker claim; that is, that it is always possible to construct alternative theories which are empirically equivalent and also share many of the characteristics we desire in scientific theories. For example, suppose that a theory T1 represents the entirety of science at a given time and that P stands for the set of all observable phenomena – observable whether "naturally" or by extension using instruments. Assume then that T2 is a rival theory that has the same consequences in P. It follows that T1 and T2 are underdetermined and – more importantly – that no amount of advance in instrumentation will change the situation, since we can always construct a similar argument.

Another instance of underdetermination to concern ourselves with is that provided by Goodman’s New Riddle of Induction, discussed when looking at confirmation. By applying predicates like grue we can find theories that agree empirically to date but make differing predictions at some point in the future. In general, weak underdetermination is the recognition of the limits of evidentialism, the notion that we hold to our ideas insofar as they are supported by evidence.

To summarise, underdetermination is almost an acceptance that we are creative in our explanations and can typically find more than one for a given puzzle. It speaks against a naive form of empiricism and is only a problem for those who suppose that there is nothing more to science and scientific theories than an appeal to data.

Confirmation

Sat, 12 Jun 2010 19:35:48 +0000

By Paul Newall (2005)

Suppose we have an idea about world and put it to the test. Our discussion of falsificationism looked at what we can conclude from a failure, but what if an experiment shows us what we expected to find? We usually say that the test has confirmed the theory, but what does this mean? There have been several approaches in the philosophy of science to understanding what confirmation involves, some with more success than others. We will examine the main candidates here.

Basic Confirmation

The easiest way to tell a story about testing scientific theories is to say that a successful trial proves that the theory was true. If we set this out in syllogistic form, we have:

If theory T is true, we would expect to note observations C;
We observe C;
Therefore, T is true.

Unfortunately, this reasoning is an example of affirming the consequent. Even if we drop the difficult issue of truth and try to say that observing C merely confirms T, we still run up against the same underlying problem: that a theory "works" is no guarantee of its accuracy. After all, it could be that something else is causing the effects we notice. For example, consider the example of Brownian motion covered when we looked at Ockham’s Razor. The phenomenological theory of gases explained the behaviour of gases and was highly confirmed by experiment but nevertheless gave way to the kinetic theory; that is, another explanation was found.

Pardoxes of Confirmation

This should not come as any surprise, however. Expecting a single successful experiment to confirm a theory so decisively is perhaps aiming too high, but another difficulty with confirmation was identified by Hempel (1937). Suppose we consider the proposition "all swans are white" (1). This is logically equivalent to the proposition "all non-white things are non-swans" (2); or, to put it another way, "if it isn’t white then it can’t be a swan". Now imagine that we notice a black raven, a creature beloved of philosophical arguments. Although it may seem that this has nothing to do with (1), it actually confirms (2): the black raven isn’t white and isn’t a swan, so (2) holds. Since (1) and (2) are logically equivalent, though, the black raven turns out to confirm that all swans are white.

Notice the way that this example was constructed: we could have chosen any number of ridiculous instances for the confirmation of (2) to arrive at the same result. It seems that (1) is thus confirmed by observations that have nothing at all to do with whiteness or being a swan. This result is paradoxical because we tend to think that a proposition like (1) is confirmed by sighting white swans, and further than the more white swans we observe the more likely (1) is to be true; but if a black raven can confirm (1) then this account seems to make little sense.

The Problem of Induction

The issue at the heart of understanding confirmation is of course the famous problem of induction, due to Hume: how can we justify an inductive inference – in the form of a general (scientific) theory – from a finite number of particular instances? A number of solutions have been proposed, including Popper’s falsificationism (claiming that scientific inference is actually deductive) and Mill’s System of Logic (1837 - actually much the same as Galileo’s and that of Aristotle and the Jesuits before him), but induction is interesting because it seems that any description of what confirmation is must rely on it. After all, if we want to say that a test has confirmed a theory in some way that we are making an inductive inference.

A more recent version of the problem is Nelson Goodman’s (1983) New Riddle of Induction. Suppose we take two propositions: "all emeralds are green" (3) and "all emeralds are grue" (4), where “grue” means green until time T and blue thereafter. Now consider what we can say about each observation we make of an emerald before time T. (3) says that we should find that each emerald is green, so a green emerald confirms it; but (4) says the same and hence seems to be confirmed as well. This is an example of underdetermination but is also another paradox of confirmation. The obvious response is to say that no one has seen any emeralds change colour in the past, nor have we heard of a reason how this could happen, but this is begging the question: if we assume that a causal link exists in the first place and hence that all emeralds are green come what may, then it is trivial to say that an instance of a green emerald confirms what is already certain.

Goodman’s own solution was linguistic, saying that the predicate green is entrenched in our language and our interaction with the world (especially when buying or talking about emeralds); but this is no solution at all, since all it does is acknowledge that we are inclined to think in a certain way without explaining whether or not we are justified in so doing. Another – more promising – possibility is to make a distinction between weak and strong confirmation, with observation and experiment never being more than a fallible form. Theoretical reduction, which proposes and explains causal mechanisms at work in predicates like greenness, gives us stronger reasons for believing that (3) is meaningful while (4) is not. This is to say that we have no idea what a grue form of science would be like – that is, how could we have a science if we had no way of knowing when emeralds would change colour or why - or how it could make any sense, and is thus a realist argument. It has the unfortunate consequence, however, of making non-scientific inferences unjustified; that is, unless we know of a theory that explains why swans are white, we have no reason at all to suppose that the next one we see will be.

Bayesian Probability Theory

Given the difficulties with these understandings of confirmation, an alternative is to appeal to probabilities instead. This is perhaps a more intuitive approach, since it aims only to say that a successful test of a theory makes it more likely. For example, suppose that someone claimed that they were friends with a certain film director and able to predict what she would be working on next. If he was correct with his first attempt, we might say it was just a lucky guess; but if he was right again on numerous occasions, we would probably think there is something to the claim after all. Indeed, the more times his guesses were accurate the more likely we would say that his being friends with her actually is – or so it seems. Can we justify this kind of thinking, though?

Bayes’ Theorem is a way of evaluating the probability of an hypothesis based on the evidence we have for it. It takes several forms but the simplest is to consider evidence e for an hypothesis h. We say that

P( h | e ) = [P( e | h ) * P(h)] / P(e) (5)

This means that the probability of the hypothesis h, given the evidence e that we have for it, is equal to the probability of the evidence given the theory multiplied by the probability of the hypothesis, all divided by the probability of the evidence itself. Sometimes this is expressed as

P( h | e * b ) = [P( e | h * b ) * P( h | b )] / P( e | b ) (6)

where the extra term b stands for the background conditions (thus P( e | h * b ) means the probability of the evidence given the hypothesis and the background conditions, and so on).

Bayesian theory is helpful because it helps us appreciate that the likelihood of an hypothesis depends on the evidence for it. The problems arise when we look at the terms on the right-hand side of (5) or (6): P(e | h) expresses the conditional probability of the evidence given the hypothesis; that is, how likely are we to find e if we suppose that h is true? Similarly, P(h) is the prior probability that the hypothesis is true, but this is precisely what we do not know and are using the evidence to evaluate. It is the assigning of these probabilities that poses the most significant challenge to Bayesian ideas.

For example, suppose we are pulling numbers out of a hat, written on slips of paper, and that the first eight have all read "10". How do we then decide what the conditional probability of the hypothesis "all the numbers read 10" is, given that these eight were? Similarly, and even before we took any pieces from the hat, how could we determine the prior probability that all would read 10? Bayesians respond that although instances like this are troublesome, typically in science we have a good idea of which probabilities to use. In the grue case, say, we would imagine that the likelihood of an emerald turning blue at some point in the future is very small indeed, so we can use Bayes theorem. Critics object that actually the Bayesian approach only addresses part of the grue problem – i.e., the hypothesis before T and not after.

Inference to the Best Explanation

An alternative method proposed by C.S. Peirce (see his Collected Papers, 1931-1958) and others is inference to the best explanation, sometimes known as abduction. A nice way to understand it is via two different metaphors: rather than science being like wandering around a beach at night, picking up "observations" to confirm our theories, instead we try to come up with the best explanation of the facts we have and then use this theory like a candle or flashlight, illuminating larger areas of the beach to see what else we can learn about it. This intuitively makes a good deal of sense: when we have the best explanation of a set of evidence, we say that the evidence confirms the theory.

There are several difficulties associated with abduction. In the first place, what do we mean by the best explanation? We could say that it is the most probable, but then we are back with Bayesianism or something similar. Also, what makes an explanation good enough? That it is able to explain the evidence is admirable, but – once again – so do others, since the theory is always underdetermined by the evidence. Moreover, sometimes scientists infer several explanations where there are competing possibilities (colour-perception models in neurophysiopsychology, for example) and sometimes they refuse to make any inference at all (the most notable instance being Bohr in his early years, when he struggled with the implications of quantum theory and steadfastly refused to take the easy road to an instrumental interpretation).

More importantly, perhaps, we recognise that we use other (non-empirical) criteria to judge how good our theories are. For example, we tend to prefer them to be parsimonious; not ad hoc; predicting novel facts about the world; and so on. Including these in a description of the "best" theory, however, is not easy; after all, there seems to be no reason why the universe should be fundamentally simple rather than complex, so which of two theories fitting these characterisations is the better one, other things being equal? It seems, then, that to be more accurate we need to replace "best explanation" with "best of the available explanations, where this option is good enough for our purposes", with the latter being open for discussion.

In summary, there are many aspects to confirmation and much debate as to which formulation is most satisfactory. Note, though, that there is no question that we do employ inductive inferences and that we regard our ideas confirmed in some way; the question is how we can justify this inevitable practice.

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Selected References:

Goodman, N., Fact, Fiction and Forecast (Cambridge, MA: Harvard University Press, 1983).
Hartshorne, C., Weiss, P. and Burks, A. (eds.), Collected Papers of Charles Sanders Peirce, 8 vols. (Cambridge, MA: Harvard University Press, 1931-1958).
Hempel, C.G., Le probl�me de la v�rit� in Theoria, 3, pp.206-246, 1937.
Mill, J.S., A System of Logic (Honolulu: University Press of the Pacific, 2002).

Theory-ladenness

Sat, 12 Jun 2010 19:31:51 +0000

By Paul Newall (2005)

According to one understanding of the so-called Galileo Affair, the old system of geocentrism was challenged by the new observations made possible by Galileo’s invention of the telescope. In general, it was believed that theories are tested against observations, so that we have a clear demarcation between theoretical and observational statements; the former confirmed or otherwise by the latter.

This picture breaks down quite quickly when we consider it in more depth. To begin with, Galileo's observations were not made via his unaided senses but through a telescope. Some of his contemporaries were extremely skeptical of this instrument; indeed, what Galileo lacked was a theory of optics to explain why those looking through his telescope could trust what they were "seeing" rather than suspecting the apparent celestial phenomena to be tricks of the lenses. Thus what occurred was not the clash of Aristotelian/Ptolemaic theory with observations but instead with Galileo's observations in light of his own optical theories (or lack thereof). We say that the observations were theory-laden.

This line of argument was originally developed in the 1950s and 60s in opposition to the positivist demarcation of observational and theoretical statements, mainly by N.R. Hanson (1958) and later Thomas S. Kuhn (1962) and Paul Feyerabend (in 1981i and 1981ii). It also found a role in critiques of falsificationism. In response it was agreed that some forms of this demarcation failed but that nevertheless there was a natural boundary between statements derived via theoretical considerations and those resulting from the unbiased experience of the world available to us through the senses. In spite of the existence of hallucinations and other sensory phenomena classified as errors (or variously as unscientific, unhealthy or delusional), it was believed that pure impressions could be received by the passive mind and hence constitute direct knowledge of the world. That is, it is possible to identify a normal cognitive process that, although vulnerable to mistakes due to mental illness and other factors, could be relied upon.

A debate took place during the 1980s between Churchland and Fodor (see their 1988 and 1986 respectively for representative instances) concerning the extent to which theory-ladenness plays a part in perception. The latter argued that a distinction should be made between perception and inference, wherein the difficulties discussed above would apply to deriving statements from our observations but not to the actual observations themselves. Churchland and others responded (see his paper A Deeper Unity in Munevar (ed.), 1991, for example) by noting that observation is not simply a matter of perception; instead, it is a cognitive achievement that involves perceiving that something is or is not the case. A number of papers in neuroscience and related areas by Churchland and others have since expanded on this insight, explaining that if our brains held no hypotheses about the world when encountering it (or, alternatively, if these hypotheses were fixed) then we would not be able to learn from new information. This is to say that observations and experiences have to be interpreted to be meaningful and it is this unavoidable involvement of a theoretical dimension – even at the level of brain functioning – that constitutes theory-ladenness. It goes all the way down, as Feyerabend would say.

To return to examples, then, even a straightforward statement such as "this lump of coal weighs one kilogram" is riddled with theory. Whether we include inference from prior experience (i.e. that the heaviness from lifting pieces of coal is conserved over time); the apparatus required to derive weights; the physical theories upon which the instruments and concepts like weight and mass are based; other theories that determine the effect (if any) on weight at different locations; and so on; we are very far indeed from a "basic" proposition.

Not surprisingly, theory-ladenness has been considered a problem because of the importance attached to experiment as an arbiter in testing and/or choosing between physical theories in science. Much discussion has taken place, particularly with regard to the so-called "experimenters’ regress" identified by Collins: the “correct” result of an experiment is one obtained via correctly functioning apparatus; but the latter is nothing more than that which gives a correct result. Similarly, how do we judge the competence of an experimenter other than by whether he or she obtains the "correct" result? For Thomson, the point was that when we talk about repeating an experiment we mean that we "repeat all the features of an experiment which a theory determines are relevant", so we find ourselves "repeat[ing] the experiment as an example of the theory." The apparent lack of any formalised rules (or demarcation criteria, yet again) to decide these issues has led to increased awareness of the importance of other factors, especially sociological ones.

If Churchland is correct about the inevitable role of theory-ladenness, however (insofar as it is what makes learning possible in the first place and our experience of the world genuinely cognitive), then it is not so much a circumstance to be lamented but a realisation that judging what there is or is not in the world by reference to passively observing it was too simplistic a hope to begin with. Lubbock's advice that "what we see depends mostly on what we look for" thus becomes not a cynical refrain but an encouragement to look again and again in different ways as part of a truly reflexive practice.

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Selected References:

Churchland, P.M., A Deeper Unity: Some Feyerabendian Themes in Neurocomputational Form
in Munevar, G. (ed.), Beyond Reason: Essays on Paul Feyerabend (Dordrecht: Kluwer, 1991M.).
Churchland, P.M., Matter and Consciousness: A Contemporary Introduction to the Philosophy of Mind (Cambridge, MA: Cambridge University Press, 1988).
Feyerabend, P.K., Realism, Rationalism, and Scientific Method: Philosophical Papers, Volume 1 (Cambridge: Cambridge University Press, 1981i).
Feyerabend, P.K., Problems of Empiricism: Philosophical Papers, Volume 2 (Cambridge: Cambridge University Press, 1981ii).
Fodor, J., Psychosemantics: The Problem of Meaning in the Philosophy of Mind (Cambridge, MA: The MIT Press, 1986).
Hanson, N.R., Patterns of Discovery (Cambridge: Cambridge University Press, 1958).
Kuhn, T.S., The Structure of Scientific Revolutions (Chicago: University of Chicago Press, 1962).

Ockham's Razor

Sat, 12 Jun 2010 16:59:16 +0000

By Paul Newall (2005)

Ockham’s Razor, otherwise called the principle of the economy of thought, is invoked often in debate, usually to discount one or more theories on the basis that another exists which is simpler or more parsimonious. In this essay we shall consider this principle, its domain of application and some associated philosophical concerns, using examples from the history of science to illustrate some of the points at issue.

The Simplest Explanation

The principle of parsimony is typically stated as Entia non sunt multiplicanda praeter necessitatem ("Entities are not to be multiplied beyond necessity"). Although referred to as Ockham’s Razor after William of Ockham, a Franciscan living at the turn of the fourteenth century, this version has not been found in any of his extant works. The closest match (Frustra fit per plura quod potest fieri per pauciora or "It is pointless to do with more what can be done with fewer") may have been written in quoting others, and indeed the general principle was common among Aristotelians. In brief, the advice is that we should not invoke entities in explaining a phenomenon or developing a theory that are not necessary to do so.

For example, some people suspect that crop circles are due in some way to extraterrestrial influence, whether directly or otherwise. Others suggest that the patterns are the work of dedicated artists or hoaxers and very much an earthly occurrence. On the face of it, then, especially given that the latter group have been able to demonstrate the construction of a crop circle, there is no need to posit aliens to account for why farmer’s fields are routinely invaded in this fashion. If we wish to hold to economy of thought, we should pick the simpler explanation.

Ockham’s Razor is a principle; that is, it does not tell us that the simplest explanation is true (or what there is); but instead that we ought to prefer it on methodological grounds. We are counselled to adopt theories which are minimally efficient, insofar as they can do the same with less. Note that there is apparently no reason why we should do so: a direct route to a destination is neither better nor worse than a diversion unless we include the criterion that we wish to get there by the most direct route (and even then it may not be, so we will return to this analogy later.) Nevertheless, it seems plain enough that we are inclined to favour the simpler explanation, other things being equal. It is this assumption that we shall now examine.

Applying Ockham’s Razor

Perhaps the best-known example of two competing theories between which a decision had to be made was the seventeenth century controversy over astronomical systems. The long-standing Ptolemaic/Aristotelian model of the heavens was challenged by the Copernicans, who insisted that heliocentrism was simpler than geocentrism. (Note that the question of geostaticism – or the fixed (or otherwise) nature of the Earth itself – was a separate issue.) Since that time much effort has gone into demonstrating (or refuting) the claim that either system was more parsimonious than the other.

Although Copernicus had believed that a sun-centred universe consisting in circular orbits was the most beautiful that could be created, he did so on the basis of thematic assumptions derived from his neo-platonic influences and not as a result of any new observations, of which there were none until some years later. (Max Jammer has shown that Copernicus’ reasoning resulted in his being faced with having to reject either geocentrism or the Aristotelian conception of space. Having no metaphysical substitute for the latter, he was forced to dispense with the former. Ptolemy had actually considered the possibility of circular motion but dismissed it precisely because it did not agree with what was seen in the night sky.) On making the change to heliocentrism, Copernicus found that he still required the assistance of devices like epicycles to save the phenomenon; that is, to make the predictions of his theory agree with what was actually discerned by astronomers. The issue of comparative simplicity has subsequently been reduced by some commentators to counting epicycles but for our purposes this is beside the point: neither the Ptolemaic nor Copernican system was empirically adequate, leading Kepler to produce another.

The basic error inherent in the counting approach is to consider theories in isolation. A theory includes a host of ancillary presuppositions and exists within a metaphysical system. A comparison with an alternative implicitly or otherwise assumes that all other things are equal (called a ceteris paribus clause in Latin) when they are not (or, at the very least, no attempt is made to show that this requirement is satisfied). Copernicus himself was wary of asserting the truth of his system and only received a copy of his De revolutionibus orbium celestium on his deathbed. When the issue was forced during the so-called "Galileo Affair", a judgement was sought between two systems whose empirical base was the same and whose practical utility was identical at that time. Galileo sought to delay any choice by invoking the Augustinian principle that it would be folly to ground theological certainties on physical propositions that may subsequently be shown to be false, but his pleas were not heard.

There are several lessons to take from this historical episode. In the first place, we have two competing theories with the same content, and thus a prime candidate for the application of Ockham’s razor. Upon consideration, however, we immediately note that the ceteris paribus clause was not satisfied, and for many reasons. The theological consequences were (ostensibly) very different; the political outcome moreso, particularly against the backdrop of the Reformation; the implications for morality were easy to predict but harder to judge; and the metaphysical fallout was just beginning to be investigated. The decision made on this basis did not count the number of postulated entities (which were the same to all intents and purposes) and did not include a conclusion on the relative economies of each theory, since they were also equivalent. In any event, Copernicanism was rejected with scarcely a mention of William of Ockham.

We know now, of course, that a variant of heliocentrism eventually won the day. Galileo’s warning to the Church was not heeded and its choice to assert the reality of geocentrism had catastrophic results for its authority and – later - its credibility. Nevertheless, the history of this change is also illustrative: at no time was there an invocation of the "decisive experiment" of myth, dreamt of by many a philosopher of science. When Foucault’s experiments with his pendulum showed the movement of the Earth, confidence in geocentrism had already been slowly eroded over the years. At the only stage in this entire episode that a comparison between rival theories had been insisted upon, the question was decided by "non-scientific" means (notwithstanding the anachronism implying the inverted commas) with Ockham’s Razor playing no part.

The general point raised by this brief study is that Copernicanism required time to develop. Attempting to make a straightforward comparison was disastrous for the Church and for astronomy (and subsequently science) in Italy. Kepler was able to refine the basic Copernican insight because the theory was not limited to the narrow domain in which it was judged.

Theories of gases

Consider now a theory, which we call T1, say, applying within a domain D. T1 predicts P while the actual state of affairs is in fact P', close to P but their difference being beyond experimental possibilities. That is, there is a difference but it is so slight that we could never notice it by investigation. In such circumstances it would be of little use to hope (or even expect) that an increase in experimental capabilities will lead to the discovery that P' actually obtains because there is no apparent need to refine T1. Suppose instead that we propose additional theories T2, T3, etc, each of which differs from T1 within D and which predicts P'. Ockham's razor cannot help us decide whether or not to pursue these new theories, but when we investigate them further we may find that T2, say, is confirmed where T1 was but also makes novel predictions not given by T1, or else suggests answers to extant problems for T1. In that case, then, we may chose to reject T1 and adopt T2, even though no refuting case has been made against T1.

Although this hypothetical example may be considered fanciful, it is illustrative of what occurred when the kinetic theory of gases was proposed in opposition to the prevailing phenomenological theory. For the phenomenological theory of gases (i.e. based on describing the behaviour of gases via the laws of thermodynamics), Brownian motion was an instance of a perpetuum mobile that refuted the second law of thermodynamics, which expressly disallows perpetual motion. (In brief, the apparently random movement of the Brownian particle seems to go on indefinitely, suggesting that somehow the particle does not run out of energy. In kinetic terms, however, we now say that it is being "bumped" by other molecules, explaining both its behaviour and where its energy comes from.) Following his studies of Brownian motion, Einstein (see the 1956 edition of his Investigations on the Theory of the Brownian Motion) was able to entirely recast the phenomenological theory in kinetic terms, in spite of having no experimental motivation beyond the known difficulties to do so; after all, the differences in temperature expected, were the kinetic theory correct, were below the range of detection of thermometers (see Furth, 1933). Nevertheless, the new theory prevailed when Einstein used his theory to derive statistical predictions for the behaviour of the Brownian particle by assuming that molecules existed and a mechanical account of the motion could be given. (Feyerabend (1963 (1999, pp.92-94)) made this argument for a different reason, which Laymon (1977) disputed). This decision could later be justified by the eventual successes of the kinetic programme, but this is only to say that parsimony was discussed after the event, if at all. The possibility of applying Ockham’s Razor was again not considered, nor could it be of any use.

The Special theory of Relativity

When Einstein published his 1905 paper on special relativity, the first response remarked on how his ideas had been decisively refuted by Kaufman's papers of that year and the next in the Annalen der Physik (in issues 19 and 20, especially his Uber die Konstitution des Electrons (1906, p.487)). Kaufman began, in italics, by saying that the "measurement results are not compatible with the Lorentz-Einstein fundamental assumptions". To see how convincing Kaufman's work was considered, we may note that Lorentz wrote to Poincaré in March of 1906, saying that his theory was "in contradiction with Kaufman's results, and I must abandon it." The latter agreed and could offer no advice. A glance through the journal and the absence of significant (indeed, any for quite some time) response shows how seriously Kaufman's objections were taken. (See Feyerabend, 1999, pp.146-148 for more detail on this and the below.)

Planck, however, was committed to Einstein's ideas because he thought their "simplicity and generality" meant that they should be preferred, even in the face of experimental refutation. He attempted to re-examine Kaufman's data and demonstrate that there were flaws, but instead he found that they were far closer to Abraham's rival theory. Thereafter he presented his findings at the Deutsche Naturvorscherversammlung in Stuttgart in September 1906, a rather amusing affair in which Abraham drew much applause by observing that since the Lorentz-Einstein theory was twice as far from Kaufman's data as his own, it followed that his theory was twice as good (Physikalische Zeitschrift 7, 1906, pp.759-761). Planck tried but ultimately failed to convince Sommerfeld, Abraham or Bucherer that Einstein's ideas should be given time to develop (ibid). Ultimately, of course, they were accepted because of their "inner consistency" (Wien, 1909) or because Kaufman's experiments lacked "the great simple universal principle" of relativity theory (von Laue - see below), so that the matter was decided well before Kaufman's results were finally shown to have been flawed (Guye and Lavanchy, 1916).

Thus we find that Einstein's ideas succeeded because of a large measure of rhetoric from him, Bohr, Planck and others, and because of a commitment to the presuppositions of relativity theory, long after there had been very little doubt (on the parts of very many great and distinguished physicists) that experimental considerations had killed it. Indeed, by 1911 von Laue was writing that "a really experimental decision between the theory of Lorentz and the Relativity Theory is indeed not to be gained; and that the first of these nevertheless had receded into the background is chiefly due to the fact that, close as it comes to the Relativity Theory, yet it lacks the great simple universal principle, the possession of which lends the Relativity Theory from the start an imposing appearance" (see Das Relativitätsprinzip, 1911). Physicists were more interested in how they could use Einstein's ideas to explain the result of the Michelson-Morley experiment, even though they were still confusing Lorentz's and Einstein's theories in 1921 significantly enough for von Laue to address it (see the fourth edition of his text, then entitled Das Relativitätstheorie as acceptance of the theory had grown and hence changed its status from a mere "principle"). As a result of these theoretical and thematic factors, D.C. Miller's later (apparent) falsification of Einstein was given very little attention at all, even though it again took a long time (almost thirty years) for Shankland to find the mistake (1955, pp.167ff). (See Holton, 1988, for more discussion of these episodes in the history of physics.)

We see, then, that even in this instance in which the notion of simplicity was relied upon throughout, no actual comparison of the number of entities or parsimony took place. The special theory was held to possess greater inherent simplicity both before and after any experiment and in spite of the negative results of Kaufman’s work.

The general case

There are two major difficulties with Ockham’s Razor. The first is that other things are rarely (if ever) equal, so the ceteris paribus clause is not satisfied. The second, perhaps still more important objection is that the unknown (or additional) entities parsed away may have explanatory power outside the domain of consideration, or they may offer further methodological suggestions which subsequently show that the utility (or even truth) granted to the former explanation was too narrow. The extra terms may be methodologically interesting and stimulating even if they turn out to be completely in error. As Niels Bohr was fond of saying, parsimony is judged after the event. It makes little methodological sense - to hammer the point home - to disallow additional entities before their consequences have been investigated; indeed, the application of parsimony in the examples we have considered above and throughout the history of science would likely have proved disastrous, at least with the benefit of hindsight (and quite plainly in the case of heliocentrism).

The lack of evidence for a posited entity is hardly a problem for scientists who are both willing and able to continue their efforts regardless. Moreover, this risks putting the cart before the horse: a theory may predict the existence of an entity for which there is no evidence but which is as a result subsequently discovered. While there may be a limitless supply of alternative hypotheses (as asserted by the strong underdetermination of theories), or at least enough to require a decision between them (even if only on practical or financial grounds), not all of them will (or may be suspected to) have interesting enough consequences to pursue. The methodological point is, once again, how can we know the utility (or truth) of apparently un-evidenced or unwarranted theories/entities before the fact? Given that so many have turned out to be of benefit in the past – or so goes the historical argument - why assume to the contrary now?

Historically (and today) theories are surrounded by anomalies and additional entities are postulated to explain them, sometimes ad hoc (thus maintaining the theory) and sometimes requiring a replacement. The resulting alternative(s) would be empirically equivalent and adequate within the domain satisfied by the current theory, so disallowing hypotheses that fail the requirement for parsimony presupposes that they will also fail to be successful. This what the Church imposed upon Galileo, and so to follow Ockham’s Razor leaves us with a dilemma: should we reject theories that appear to violate parsimony and risk stifling (or ending) their development, which may subsequently show otherwise; or should we instead reject the requirement for parsimony and accept that matters are more complex than the shortest route being the one to prefer?

If we return to our T1 and T2, we can note that T1 may employ different assumptions to T2 such that a straightforward comparison is not possible (Berkeley's idealism being a good example). Moreover, two hypotheses may be successful in different domains but mutually exclusive within their intersection, if there is one (complementarity, for instance). The believer in God or in aliens declaring an agency other than man was responsible for a phenomenon does not make a straightforward choice but involves their additional entity as part of an entire worldview (incorporating the existence of God or extraterrestrials respectively) which also explains or makes sense of a whole range of phenomena. The ceteris paribus clause here can also turn out to be have failed: perhaps the confirming instances of T1 are apparently refuted (as with special relativity) but the addition of the further assumptions can explain these anomalies, or else neither theory may be satisfactory and the proper response might be to withhold judgment. T2 may in addition have greater predictive or explanatory (or both) power outside the domain of comparison, making the evaluation within D an interesting but not particularly devastating factor. Rather than straightforwardly dismissing T2 because of its auxiliary (and apparently unnecessary) assumptions, it may instead make methodological sense to investigate what consequences these have.

Moving beyond any actual results or possibility thereof, the additional entities rejected by parsimony may not explain any other data in further domains but still provide a stimulus to work which subsequently uncovers further domains in which they are necessary, or which show the previous theory to have been but an approximation. In short, epistemological considerations are not sufficient to choose between theories and cannot be expected to account for scientific practice. While methodological concerns are also not necessarily of ultimate import, scientists appear to use them more as they press on, blithely unaware of or unconcerned with the philosophical ideas that are intended to provide them with guidance. This is that element of guesswork and certainty of resolve which prompts scientists to continue to work on ideas rejected by many of their contemporaries (plate tectonics, say, or Pauli’s positing of the neutrino), perhaps reminded of the changing fortunes of atomism over millennia.

Another way to introduce or justify Ockham’s Razor is to assert that parsimonious theories are more likely to be correct. This is a problematic claim. Suppose we take the case of a theory which is regarded by all as highly successful, but which relies upon unobservable entities (such as sub-atomic particles, say). Is the theory true or just a useful instrument? Is it more parsimonious to suppose that these entities do or do not exist? In the absence of an ability to divine the fortunes of a theory in the years to come (or, in the case of atomism, the thousands of years), how are we to decide? To assume, as many apparently do, that parsimony is important because the universe is fundamentally simple, rather than complex (hence the search for grand theories, underlying all others), merely begs the question.

To get where we are going

To summarise our discussion, then, the important point which renders parsimony methodologically unhelpful, if not explicitly detrimental, is that the consequences of additional entities or assumptions are impossible to state a priori. Since science is never completed, we are always in the position of before and never get to the after, which Bohr claimed was the only place parsimony could be introduced, much less judged.

Selected References:

Einstein, A., Investigations on the Theory of the Brownian Motion (New York: Dover, 1956).
Einstein, A., Über das Relativitätprinzip und die aus demselben gezogene Folgerungen in Jahrbuch der Radioaktivität, vol. 4, 1907.
Feyerabend, P.K., Knowledge, Science and Relativism (Cambridge: Cambridge University Press, 1999).
F�rth, R., Über einige Beziehungen zwischen klassicher Statistik und Quantenmechanik in Zeitschrift für Physik, vol. 81, 1993.
Guye, C.-E. and Lavanchy, C., Verification experimentale de la
formule de Lorentz-Einstein par les rayons cathodiques de grande vitesse in Archives des sciences physiques et naturelles, 42: 286–299, 353–373, 441–448, 1916.
Holton, G., Thematic Origins of Scientific Thought (Cambridge: Harvard University Press, 1988).
Kaufman, W., Über die Konstitution des Electrons in Annalen der Physik, vol. 19, 1906.
Kuhn, T.S., The Copernican Revolution: Planetary Astronomy in the Development of Western Thought (Cambridge: Harvard University Press, 1957).
Laue, M. von, Das Relativitätsprinzip (Braunschweig: Friedrich Vieweg & Son, 1911).
Laymon, R., Feyerabend, Brownian Motion and the Hiddenness of Refuting Facts in Philosophy of Science, 44, 225-247, 1977.
Physikalische Zeitschrift, 7, pp.759-761, 1906.
Shankland, R.S., A New Analysis of the Interferometer Observations of Dayton C. Miller in Reviews of Modern Physics, vol. 31, 1963.
Wien, W., Über Elektronen (Leipzig: B.G. Teubner, 1909).

The mechanical philosophy and God

Sat, 12 Jun 2010 16:56:23 +0000

By Paul Newall (2007)

In his famous work The Mechanization of the World Picture, E.J. Dijksterhuis described in great detail the development of the so-called mechanical philosophy from its origins in antiquity with the Greeks to Newton in more modern times. In its earlier incarnations there were convincing enough counter-arguments that it was not a serious concern to ideas about God. With the rise of experiment as a check on theory, however, mechanical philosophy began to seem more tenable and its possible clash with theological matters more pressing.

Potential problems with the mechanical philosophy were quickly seen by Mersenne, who worried that it might run up against theology and imply that there was no room for miracles. University tutors also became concerned at the consequences that their students were drawing from Descartes' thinking. Nevertheless, the principle difficulty was with God's freedom to act in the world and that free will He had supposedly granted to his creation: if the universe was explicable in mechanical terms – that is, as a machine, running like clockwork, whether crafted by God as great artificer or not – then how could men avoid the inevitable result of the playing out of that design and how could God change it without ruining the structure?

Mersenne had originally favoured mechanistic ideas because he had realised that some form of natural order would be necessary before there could be a miracle that is contrary to nature. For this reason, he advocated the study of nature and the determination of natural laws, but it was easy for critics to associate the supposedly atheistic atomism of the early Greeks with the mechanical philosophy and it was a small matter to move from mechanistic ideas being able to explain the workings of the universe to there being no place left for God, as Laplace would famously remark. Both Mersenne and Descartes believed that God was inscrutable, with the ultimate essence of things forever beyond our capacities; even so, if the mechanistic philosophy was proving valuable in understanding the natural world and the supernatural lies out of reach then it seemed to some that the mechanists were contributing, indirectly or otherwise, to the minimisation or death of God.

How, then, could the mechanistic philosophy be accommodated with a God acting in the world? Descartes chose to ignore the problem, supposing instead that there was no intersection between the domains of faith and nature. This undermined the doctrine of the Eucharist, though, and hence was not considered an option. In an attempt to avoid the more unpalatable consequences of Descartes' work, Malebranche devised the notion of occasionalism, according to which God's direct intervention could be invoked whenever sense-perception was involved; that is, a God actively taking part in His creation at all times and sustaining it. Since it was believed that Descartes' philosophy could explain the workings of nature without any reference to God, his works were placed on the Index of Forbidden Books in 1663, followed by a Royal ban on the teaching of his ideas in French universities.

Gassendi took a rather different approach, believing that he could rehabilitate the doctrine of atomism in a way that would render it compatible with Christian theology; in effect, trying to reduce the barriers between science and religion rather than hold them to be immovable like Descartes. In modern parlance, Gassendi was an instrumentalist, believing that empirical adequacy was the aim of science. Knowledge of causes would remain beyond us, so he defended atomism because it provided a plausible account of the phenomena that Aristotelianism could not; the question of whether God had no role to play in his mechanistic world therefore did not arise, and the issue of whether atomism was "true" or not would not concern him. Some philosophers of science have employed a similar understanding today.

Pascal was deeply interested in experiment and the mechanical philosophy but nevertheless maintained a separation between his work and his theology, demarcating them clearly. Although he believed that the work of God was evident in nature, he held that God Himself was hidden therein rather than manifest. No amount of study of the natural world – on the basis of the mechanistic philosophy or otherwise - could prove the existence of God, then, but neither could it disprove or caution against faith. Pascal, much like Gassendi, was not concerned to show how God interacted with the world because – for both – their understanding of that world rendered the problematic aspects of mechanism moot.

Steno was of a different persuasion: he felt that there was and could be no conflict at all between science and religion. The workings of nature – in his case, geology – could be studied to supplement the Scriptural account; where nature was silent we can appeal to the Bible and where neither tell us anything we can say nothing. He insisted that nature and Scripture could never be in disagreement.

Looking at these five illustrative examples of French natural philosophers we thus find that none of them seem to have exhibited much concern about the compatibility of God with the mechanistic philosophy. Mersenne worried that it might find use in atheistic thinking but felt God to be beyond argument regardless. Descartes ignored the issue and Gassendi did not find there to be a problem at all, if the early atomists were understood correctly. For Pascal, God was hidden and thus under no threat from any implications of experiment or philosophy, and for Steno there was no incompatibility at all. What was never at issue was the belief in God of any of them or the possibility that mechanism might lead to a diminishing of God. They wanted to use the analogy of the clockwork universe to give greater glory to God by coming to know His work, and it is therefore something of an historical irony that those who did most to develop the mechanical philosophy did so in the belief that they were buttressing belief in God.

The issue is subtler, though. Looking again at Mersenne, we find that he was actually concerned to delimit the natural in response to Protestant criticisms that the Catholic Church used miracles to convert people. Mersenne believed in both God and miracles and wanted to employ mechanistic philosophy to show how the former worked through the latter and hence answer the Protestants. To suppose that he found mechanism convincing and then worried that there might be no place left for God is to misunderstand his intent. The mechanistic world would not exclude God or miracles; instead, it would help understand when a true miracle occurred and when it had not. (Note that this is the same motivation that lay behind research into the praeternatural in demonology.)

Descartes was also pursuing a different tack to that we might suppose on a cursory reading. He wanted to emphasise the uniqueness of man by showing him to differ from the rest of creation by the existence of his immortal soul. To do so, he used the mechanistic philosophy to demonstrate that all other regions of the universe, particularly animals, could be understood as machines, however complex. He employed mechanism to make theological points and support the activity of the divine in the world, so it is little wonder that he did not see the consequences that others found in his work. We have already seen that Gassendi felt the question to be one of correctly appreciating what the atomists meant and that Pascal and Steno had nothing to be worried about. For his part, Dijksterhuis saw no link between atomism and the mechanical philosophy, insisting that "a machine presupposes a conscious and intelligent maker who has constructed it and makes it operate to realize a particular object. It is hardly possible to maintain a conception that differs more widely from the worldview of Democritean atomism."

In summary, the issue seems to be that concern at the mechanistic philosophy was on the part of others - those who had read the French natural philosophers considered here but not sufficiently understood their motives and purposes. Leaving these out and considering the thinkers above as examples of mechanistic philosophers is therefore a huge oversimplification; it would perhaps be more accurate to call them natural philosophers who employed mechanism to achieve ends that were their own and not forced upon them by it. Mechanism suited their theological ideas and what they hoped to achieve in their endeavour to bring glory to God.

Falsificationism

Sat, 12 Jun 2010 16:54:05 +0000

By Paul Newall (2005)

This short essay discusses the various forms of falsificationism, particularly insofar as it functions as a proposed answer to the demarcation problem; that is, the search for a means to distinguish between science and non-science.

Dogmatic Falsificationism

The dogmatic (sometimes called naturalistic) version of falsificationism is at once the easiest to understand and (apparently) the most straightforward. The way to demarcate between theories is to call scientific those for which we can specify (beforehand) one or more potential falsifiers; that is, an experiment with a particular result that would cause us to give up our theory. The most common example of this approach is the proposition "all swans are white": this can never be proven, since that would require checking each and every swan anywhere; but it can be disproven by finding a single instance of a non-white swan.

A theory is scientific, then, if we can say what would possibly cause us to reject it. This seems a reasonable approach to take because if there were no circumstances that could ever lead us to reject the theory, it would be uninteresting; after all, why bother investigating a theory that cannot be wrong and is therefore already true? We could just get on with more important things, like rugby.

For the dogmatic falsificationist, this understanding helps to make sense of what goes on in science. Although a theory is never proven, if we can falsify it then we force ourselves to look again and come up with a better one. This is also unproven but an improvement on the last; and so it goes. Lakatos referred to the illustrative progression from Descartes theory of gravity, through Newton’s, to Einstein’s. As the first was refuted, the second came along and was able to explain the observed phenomena without falling victim to the same difficulties. Eventually it was also falsified but Einstein was able to do likewise again, explaining what went before but without the flaws. Falsification thus demarcates between scientific and non-scientific theories and helps account for the development of scientific theories.

Sadly, it does no such thing and it was not long before the flaws were demonstrated. There were three main concerns. Firstly, there was a reliance on a separation between observational and theoretical propositions. The latter would be a particular theory of gravity, say, while the former would be the observations that are supposed to potentially falsify it. Unfortunately this distinction is untenable. To take an example, consider the famous Tower Argument used by geokineticists and geostaticists alike (that is, those who, in Galileo’s time, held that the earth was or was not in motion, respectively). By dropping a stone from a tower, it was supposed that it could be shown whether or not the Earth was revolving as some claimed: if the Earth was in motion, the stone should fall some distance away from the tower; if not, it should land at the base. The theory was thus to be tested by observation, but the problem came when interpreting what had occurred. When the stone did fall at or near the base of the tower (allowing for experimenter error), the geostaticists remarked that this was what predicted by their theory. In like fashion, the geokineticists also expected the stone to fall at the base because they held that everything on the Earth was moving with it, including the stone and the air through which it fell. Hence we see that there was no observational statement without the theories to interpret them. This is an instance of the more general theory-ladenness of observational terms; subsequent study has shown that there can be no (theory-)neutral observational terms because we do not just passively experience the world but actively encounter it and can choose different ways to do so.

Secondly, there was a logical concern: no proposition can ever be proven by experiment. This basic result has apparently caused much confusion but it is the very difficulty that falsification was proposed to address; namely, that no proposition could ever be proven, hence the effort to disprove them instead. More generally, this is an instance of the problem of inductive logic or the knowledge that logical relations like proof are between propositions, not facts and propositions. Although falsification was supposed to avoid this difficulty by proceeding deductively instead of inductively, in order to call a theory disproven we have to rely on an experiment proving another theory – the negation of the theory under consideration – which is precisely what we agreed could not be done.

The third and last difficulty was even more severe. When we test a theory by experiment, we do not do so in isolation. Instead, what is actually tested is the conjunction of the theory with a ceteris paribus clause (a Latin term meaning "all other things being equal"). Even if we allow that the first two problems are surmountable, then, we can always dodge a falsification by saying that the ceteris paribus clause was refuted and change it for another, thereby leaving the theory intact. This is exactly what was done with the Tower Argument, for example: the experiment designed to disprove the motion of the Earth was actually testing the theory "a stone dropped from a tower on a static earth will fall at the base, assuming everything else on the Earth is not moving with it". The geostaticists thus immediately said that the italicised ceteris paribus clause has been falsified, not the motion of the Earth. Lakatos gave another example of an astronomical theory that predicts certain behaviour in the heavens, which is actually not observed. Rather than consider his theory falsified, the theorist then says that there must be another body invisible to the naked eye causing the anomalous effects seen. Even when a new telescope is invented and this is no longer tenable, the theorist appeals to the influence of a magnetic field nearby; and so it goes, each new ceteris paribus clause saving the theory from falsification. These auxiliary hypotheses can always prevent the conclusion that the general theory has been falsified, so dogmatic falsificationism collapses.

Methodological Falsificationism

If all theories are thus equally disproven then all scientific theories are fallible and we are no closer to solving the demarcation problem or characterising what makes a proposition scientific. This unpalatable conclusion brings us to the second form of falsificationism: methodological. The falsificationist now makes the same basic assumptions as his or her dogmatic colleague but calls them tentative – "piles driven into a swamp", as Popper put it. Relying on a set of supposedly unproblematic propositions, which he or she accepts tentatively, the methodological falsificationist proceeds as before to try to falsify theories. He or she is thus a conventionalist in that certain propositions are taken as basic and used to build a foundation of scientific theories upon. Methodological falsificationism suggests taking some things as given and seeing what happens when we test other theories thereafter; in a word, it advocates risky decisions.

We can see this at once when we ask what we are to do when a theory is ostensibly falsified. It could be that the theory is false, or that the ceteris parisbus is, or even that one or more of the "basic" propositions assumed by convention are. Although the choice we make could be wrong, the methodological falsificationist sees this as a matter of the lesser of two evils. Dogmatic falsificationism was a dead-end and hence some bold choices need to be made. The chance of rejecting a true theory as falsified is one to be taken in order to allow the possibility of progress; that is, a choice is made between a brand of falsificationism that may not work and giving up completely in favour of irrationalism and an inability to give any justification for theories. As Lakatos put it, it is "a game in which one has little hopes of winning" but he or she believes "it is still better to play than give up."

It is difficult to critique methodological falsificationism for the simple reason that it is unfalsifiable. What should concern us most is that the history of science gives little indication of having followed anything like a methodological falsificationist approach. Indeed, and as many studies have shown, scientists of the past (and still today) tended to be reluctant to give up theories that we would have to call falsified in the methodological sense; and very often it turned out that they were correct to do so (when seen from our later perspective). This tenacity in the face of apparent adversity – such as when Einstein dismissed "verification through little effect" when his special theory of relativity was falsified by Kaufman’s results – is reinforced by the commitment to the themata that Holton has shown characterise scientists' unwillingness to give up their fundamental conceptions of how the universe is. (For a critique of a potential response to historical arguments, see here.)

The study of the history of science leaves us with a stark choice: either we have to give up the attempt to provide a rational account of how science worked and works (looking for alternatives as Kuhn did), or we must try to reduce in some way the reliance on conventionalist "basic" propositions in methodological falsification and try again.

Sophisticated Falsificationism

Popper attempted to do this by conceiving a sophisiticated version of falsification that held a theory T1 to be falsified only if the following three conditions were satisfied:

There exists a theory T2 that has excess empirical content; that is, it predicts novel facts – new ones not predicted by T1;
T2 explains everything that was previously explained by T1; and
Some of these new predictions have been confirmed by experiment.

It is thus not enough to find a falsifier to reject T1. Sophisticated falsificationism takes us away from making decisions about theories in isolation and towards considering them in company with others. A theory is not to be rejected as falsified until a better one comes along. Although we might find that a number of experiments are conflicting with a particular theory, we know from our previous considerations that this is never enough to dismiss it. Instead, we wait until a new theory is found which tells us the same things as the old one but without the difficulties (some or all). This gives us a notion of growth or development of theories in place of the dogmatic falsificationism that either accepts or rejects them in single instances. It also means that the so-called "crucial experiment" of dogmatic falsificationism – one that decides the issue at a stroke – is superseded by the realisation that no experiment can be crucial, unless interpreted as such after the event in light of a new theory for which it offers corroboration. Finally, it shows that the idea of proliferating theories (trying lots of alternatives) is important to sophisticated falsificationism as it was not at all for the dogmatic version.

To go back to an earlier example, then, what made Einstein’s theory of gravity "better" than Newton’s was not that one was falsified while the other was not, but instead that Einstein’s explained everything that the earlier theory did while at the same time offering new predictions, some of which were confirmed (such as Eddington’s expedition to observe the eclipse of the sun in 1916).

The conflict in science is thus not between theories and experiments but always between rival theories. The problem with sophisticated falsification, however, arises from the fact that it is always a series of theories that are consequently referred to as scientific or non-scientific and never a single theory on its own. Where we have two incompatible theories, we may try to replace one with the other, and vice versa, in order to see which (if either) provides the greatest increase in empirical content; but we must fall back on the conventionalist aspects of methodological falsificationism or the untenable assumptions of dogmatic falsificationism in order to ultimately make a choice. After all, calling novel facts corroborated presupposes a clear demarcation between observational and theoretical terms and also that we have a straightforward situation in which no anomalies are involved – both decisions of convention as to what constitutes "basic" or "background" knowledge when undertaking the process. We have the additional difficulty of not knowing whether a potential falsifier refers to the theory being tested – the explanatory theory – or the underlying one(s) used to make sense of it – the interpretive theory. If we can satisfy the requirements of sophisticated falsificationism, which should we reject? Propositions are also no more proven by experiment for sophisticated falsificationism than they were for the dogmatic version, while we can make the same mistakes in rejecting true theories when we assume that excess empirical content has been demonstrated – not least because a different ceteris paribus clause may have new consequences that can be tested. Finally, we are still no closer to explicating the tenacity of theories, even when the conditions of sophisticated falsificationism would have us conclude them falsified, which we again find in the history of science.

In summary, then, falsificationism in its various forms is an interesting idea but insufficient either to characterise science or solve the demarcation problem. It suffers from a series of logical and philosophical difficulties that should perhaps give us pause if hoping to find a single answer to what makes good science and what does not.

Selected References:

Feyerabend, P.K., Against Method (London: Verso, 1975).
Kuhn, T.S., The Structure of Scientific Revolutions (Chicago: University of Chicago Press, 1962).
Lakatos, I., The methodology of scientific research programmes (Cambridge: Cambridge University Press, 1978).
Popper, K.R., The Logic of Scientific Discovery (New York: Basic Books, 1959).