The final aspect of the theoryladenness arguments that I will consider is the most important. Kuhn and others have argued that even the experiences themselves that a person has are influenced by their beliefs, including their theories. Not just the use of observation reports in assessing theories, and not just the linguistic form of the reports are affected, but the perceptual experiences themselves are. There is no stage in the processes of observation in science where theories do not play a role.
When giving these arguments, Kuhn and others liked to use the results of psychological research in the middle of the twentieth century. This research was taken to refute a "passive" view of perception and replace it with a view holding that perception is active and intelligent. Psychologists emphasized the multiple ways in which a pattern of stimulation on the retina could be caused by objects in the world. If there are multiple possibilities, then theoretical assumptions must be used by the visual system to make a choice (Gregory 1970).
This kind of theoryladenness argument was attacked by Jerry Fodor in a very convincing (and very funny) 1984 article called "Observation Reconsidered" My reply to the argument largely follows his. As in the case of the influence of theory on observational language, everything hinges on which theories affect observation and how they affect it.
Fodor turned the tables on some theoryladenness arguments via a discussion of perceptual illusions of the kind often discussed in psychology textbooks. Consider the Muller-Lyer illusion, represented in figure i o. I. The two lines are the same length, although we tend to see the lower one as longer than the upper one. According to psychology, the illusion is brought about by the unconscious use of background assumptions in the processing of visual inputs. People have taken this result to show a kind of theory ladenness in perception; we do not realize it, but our general and implicit beliefs about the world are affecting what we see.
Fig. i o. i
The Muller-Lyer illusion
But Fodor then notes that although it is true that the illusions seem to be produced by the effects of unconscious theory, some pieces of theory or background knowledge seem to have no effect on perception. Most notably, the illusion is not affected by the knowledge that it is an illusion, or by knowledge of the theory of illusions. Those pieces of background knowledge do not make the illusion go away. We seem to have a situation in which the mechanisms of perception are influenced by some theories and not others. And the theories that do have this effect are not high-level scientific theories. They are low-level sets of assumptions about the physical layout of the world-the three-dimensional nature of space, the effect of distance on apparent size, and so on.
Fodor links his argument to a research program in psychology that posits modules in the explanation of perception and some other tasks (Fodor 1983). Modules are automatic, innate pieces of mental machinery that do their processing unconsciously and make use of a fixed subset of a person's background knowledge. In perception, modules send their output to the "central" cognitive mechanisms. These central mechanisms have access to all a person's theories and ideas when working out what to do with the observation. So although the later stages of responding to observation are affected, in principle, by all the theories a person might have, the output of the perceptual module is not. The module's operation-which determines how things seem to a person-is not biased by whether the person accepts one scientific theory or another.
As Fodor says, this does not solve the entire problem of the role of observation in testing. Even if observation itself is not biased by commitments to scientific theories, as has been alleged, there is still the issue of what a person does with the observation. That takes us back to the problem of holism about testing.
Not all the problems have been solved, but we have made progress. And I think it is clear how this discussion provides support for a naturalistic approach to philosophy of science. Observation is a natural phenomenon, studied by fields like psychology and psychophysics. Those disciplines tell us what perceptual mechanisms are like and what kind of connection we have to the world via these mechanisms. Naturalistic philosophers can put these results to use in working out how observation operates in science generally.
There are two general sets of questions about observation that we need to answer.
i. To what extent is observation a reliable way of forming true beliefs about what is going on in the world? When is observation using ordinary human senses reliable, and when is it not?
z. Is observation neutral between competing theories of the kind we wish to test in science? Can people with very different theoretical commitments agree about what has been observed? That is, does observation provide an intersubjective basis for theory choice?
These two sets of issues are distinct, but they are connected in complicated ways. For example, if we have reason to think that observation using ordinary human senses is very reliable in normal conditions, then we can expect a wide range of people to agree when they are looking at the same thing in normal conditions. This claim could be hedged more, but the basic idea is clear. Reliable senses shared across all normal humans can be expected to deliver consensus. But it is also possible that we could have wide agreement without reliability; we might all be deluded in the same way. Some philosophers have thought that color vision is like this. Colors are not really "out there" in the world, even if we all experience them that way.
In order to assess whether observation is neutral between competing theories, the kind of evidence that Fodor presents in his 1984 paper is relevant. Although his arguments are rather convincing, the important thing here is not whether a "modular" theory of perception is ultimately right. The important thing is to see what kind of scientific evidence is relevant for settling the question. In order to work out whether observation in scientific communities is affected by theoretical differences in a way that threatens empiricism, we need to work out what human perceptual mechanisms are like, whether they tend to be similar in all normal humans, and what role high-level scientific beliefs have in the process of observation. This kind of evidence does not itself settle whether observation is a reliable way of forming true beliefs about what is going on in the world. But that is something that can be investigated systematically by psychology and psychophysics.
Note that our perceptual mechanisms might use low-level theories in a way that makes perception reliable without the low-level theories themselves being true. What we are trying to assess is the reliability of observation reports themselves. We might have built into our brains something like Euclidean geometry, which is not strictly true of our universe, but which is used in such a way that we almost always end up with true observational judgments. Note that the Euclidean habits we have for interpreting space did not prevent us from revising the scientific belief that space strictly fits Euclidean geometry, as Einstein did in his theory of General Relativity.
I will finish this section by starting to sketch a version of empiricism that follows a naturalistic approach to the role of observation. This will be a recurring theme in the rest of the book.
We ask, What is the role of observation in science? To answer this, we need first to understand the actual role of observation in the sociological patterns of scientific activity. How is observation used as a resource in science? How is it used in the settlement of controversies? Then we can start to feed in results from the scientific study of observation. We ask, Given the kind of connection to the world that observation provides, and given the role of observation in science, what kind of contact does science itself have with the world? If observation is the channel by which theory makes contact with reality, what kind of channel is it? That is a question that we can only answer by drawing on the empirical sciences that deal with observation and perception.
If empiricism about science is vindicated by the answers to these questions, it will be a form of empiricism that differs from traditional forms. Observation is a form of physical contact between our minds and the world. This contact is the produ
ct of evolution, and it has whatever degree of reliability it has because of our evolutionary history and the contingent relationships between our structure and that of our surroundings. Science is an attempt to exploit this contact between our minds and the world, and science is also motivated by the limitations that result from our relations to the world; we need science because much of the world is not accessible to ordinary observation. Science works by taking theoretical ideas and trying to find ways to expose them to observation. The scientific strategy is to construe ideas, to embed them in surrounding conceptual frameworks, and to develop them, in such a way that this exposure is possible even in the case of the most general and ambitious hypotheses about the universe. That view is a kind of empiricism, and I think we can be optimistic about that kind of empiricism. This is a form of empiricism in which naturalism is, in a sense, primary. The advantages of empiricist philosophical ideas are not shown or established by philosophy alone.
Further Reading
The history of naturalistic philosophy is discussed in Kitcher 1992.. Kornblith's Naturalizing Epistemology (1994) is a good collection of papers on the topic, including Quine's classics. Dewey's most important naturalistic work is his Experience and Nature (192.9). Callebaut's Taking the Naturalistic Turn (1993) is an unusual exploration of naturalism based on interviews; his idea of who is a naturalist is also a bit unusual in some cases. For normative naturalism, see Laudan 1987. For good examples of naturalistic work in the philosophy of mind, see Dennett 1978, Fodor 1981, Stich 1983, and Dretske 1988.
Fodor's 1984 paper on observation is the subject of a response in the journal Philosophy of Science by Paul Churchland (1988). Fodor also replied in the same issue. See also Bishop 1992. See Giere 1988 for a treatment of various other issues in philosophy of science using a "cognitive" approach that draws on psychology.
What is good for General Motors is not always good for the nation, but once science is properly understood, it turns out that what is good for the individual scientist is by and large good for science.
DAVID HULL, Science as a Process
11.1 Science as a Process
Traditional empiricism neglected the social structure of science; naturalistic philosophy has tried to avoid this mistake.
David Hull's sprawling Science as a Process (1988), the source of the epigraph above, is the product of decades that Hull spent observing and interacting with biologists, especially the community of biologists who study systematics, the classification of organisms.
Hull's story begins with a fairly commonsense picture of both science and scientists. Scientists are curious about the world, as many other people are. Individual scientists make their way into a social structure that puts this curiosity to work and does so via empirical testing. So far this does not tell us much. But Hull then argues that what makes science special is an unusually good relationship between the motivations and goals of the individual scientist, on one hand, and the goals of science as a whole, on the other.
Is science a fundamentally cooperative enterprise, or is it a fundamentally competitive one in which scientists are out for personal advancement? According to Hull (and also Merton), science runs on a combination of cooperation and competition. Neither is fundamental, and the special features of science are due to an interaction between the two. This interaction arises from the reward system found in science and the context in which the reward system operates.
Hull argues that the main professional motivation for individual scientists is the desire for recognition. And one kind of recognition is most relevant: use. Scientists want other scientists to use their work, giving credit when they do so. Clearly Hull is close to Merton here, as he acknowledges. As we saw in chapter 8, Merton argued that recognition is the basic reward in science. There might be some differences, however. Hull stresses the desire to have one's ideas used; Merton stresses being recognized as the first to come up with an idea. Often these will go together, but not always. In Hull's view but not Merton's, if a scientist's version of an idea is used because it is especially convenient, even though it was not the first, that counts as a real reward. For Hull, being used and cited matters more than anything else.
What generates the distinctive features of science, as Hull sees it, is this reward system operating in a special context. Each scientist inherits the ideas and methods of her or his field from earlier workers. Of course, an individual might revolutionize the field, but even revolutionary work starts out from an inherited context. Individual scientists cannot do anything significant without entering a system of cooperation and trust. You can't make a contribution of your own without using the work of others. And in order to use the work of others in ways that provide support for what you are doing, you need to give citations. So the desire to do work that is used requires using, and citing, the work of others. Scientists trade credit for support, and they do so in the hope that others will do the same for them. This reciprocation is not primarily a matter of goodwill (although that can be a factor); it results from a special kind of self-interest.
Traditional descriptions of science often stress the replicability of results. A result is not trustworthy if only one lab seems able to produce it. But as Hull emphasizes, no one has the time to do much of this replication and checking. The checking that actually occurs is a consequence of the desire to have one's work used. In order to do work that others will use, you need to ensure that the work that you rely on can be trusted. So those who check and attempt to replicate results will often be those who need to know whether they can rely on those ideas. Another kind of person who will be motivated to engage in rigorous checking will be someone whose own work is either discredited or made less important by a piece of new work. Hull also argues that the reason why fraud in science is so much more serious a crime than theft, even in cases where public well-being is not affected, has to do with these sorts of factors. In a case of theft or plagiarism, the only person harmed is the one stolen from. But when a case of fraud is discovered, all the scientists who used the fraudulent work will find their work on that topic deemed unreliable, and their work will not be used.
So the desire to have one's work used generates many other features of science-the elaborate networks of citation, the real but selective checking of others' results, the relative seriousness of fraud and theft. And Hull argues that although this system malfunctions on occasion, the general result is a harmonious relationship between the behavior of individual workers and the goals of science as a whole. Cooperation and teamwork is common. Hypotheses are scrutinized closely. Idle speculation and shoddy work are discouraged. Ideas are shared freely (though not before they are in publishable form). Work produced by those who are low on the totem pole is taken seriously (especially by those whose own projects might be helped or harmed).
A number of philosophers and scientists have been attracted to a picture of science as a dialogue between an imaginative voice and a critical voice, between the speculative and the hard-headed. Popper is an example. This is an appealing picture, but why should this dialogue actually occur? Hull aims to give us a mechanism. And a key part of the mechanism is the distribution of roles across different people. In contrast to Popper, Hull argues that there is no need for individual scientists to take a cautious and skeptical attitude toward their own work; others will do this for them.
Back in chapter 6, I discussed the "invisible hand" structure of Kuhns account of science. I made an analogy to Adam Smith's famous defense of market economies, which argued that a collection of selfish individuals interacting in a market tends to produce a good outcome for everyone. Kuhn's analysis of science sees a degree of individual-level dogmatism as contributing to openness at the level of science as a whole. In Smith and Kuhn we have a surprising explanatory relationship between individual-level properties and the properties of the whole. Hull's picture of science has some similarity to these cases, but as he says, the hand is not really hidden or "invisible" in the story he tells. The relationship bet
ween individual and grouplevel properties is not so unexpected.
So far we have looked at the consequences of the structure of reward and motivation in science. But why do scientists want to have their work used in the way Hull describes? This question is related to another: why has the social structure that Hull describes arisen so rarely, across the range of different communities that have wanted to understand the world?
Hull says that he assumes that both curiosity and a desire for recognition are fairly basic human motivations. But, I suggest, a desire for the specific kind of credit found in science is surely more unusual. What we seem to have is a situation in which a basic human desire for credit is shaped by the internal culture of science into a very specific desire for recognition in the form of use. More accurately, we should expect both some shaping and some selection here; individuals who do not find the scientific reward system satisfying might never finish graduate school.
Hull and Merton both look at possible roles for broader cultural features here. Modern science developed in European societies that were comfortable with the ideas of individual competition and credit. The reward system found in science was a fairly early invention. When the French Academy was founded in the seventeenth century, its members initially tried to handle credit in a communal way, but this did not work, so they switched quickly to a more individualistic approach. The Royal Society of London, under its skillful first secretary, Henry Oldenburg, used rapid publication in the Proceedings to allocate credit and to encourage people to share their ideas. Oldenburg's system, which also included anonymous refereeing of papers, is basically what has come down to us today.
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