DAVID J. BULLER
Department of Philosophy
Northern Illinois University
DeKalb, IL 60115
Abstract. The idea that human cognitive capacities are explainable by computational models is often conjoined with the idea that, while the states postulated by such models are in fact realized by brain states, there are no type-type correlations between the states postulated by computational models and brain states (a corollary of token physicalism). I argue that these ideas are not jointly tenable. I discuss the kinds of empirical evidence available to cognitive scientists for (dis)confirming computational models of cognition and argue that none of these kinds of evidence can be relevant to a choice among competing computational models unless there are in fact type-type correlations between the states postulated by computational models and brain states. Thus, I conclude, research into the computational procedures employed in human cognition must be conducted hand-in-hand with research into the brain processes which realize those procedures.
Key Words. confirmation,
computational models, weak/strong equivalence, token/type physicalism,
relevant evidence, relative complexity evidence, processing time measures,
The idea that the human cognitive system is a physical symbol system has motivated much of the work in, and most of the philosophical interpretation of, cognitive science. And the by-now-standard way of explaining what this idea involves is the Tri-Level or Tri-Stance Story.1 In a highly abridged form, the story goes something like this. Physical symbol systems can be described at three different levels. First, since they are physical systems, there is a description of their states in the vocabulary of physics and one can explain and predict (at least some of) their state transitions by subsumption under natural law.2 Second, they are such that (at least some of) their physical states instantiate symbol tokens,3 and transitions among these states are describable as formal or syntactic operations (computations) performed on these symbol tokens. And, third, they are such that, when the syntactic relations among (at least some of) their symbol states are isomorphic to semantic relations among sentences of some language, those symbol states are interpretable as possessing semantic properties identical to those of the sentences of that language;4 consequently, the transitions among those symbol states of the system can be described in terms of the semantic relations among the interpreting sentences, i.e. the system can be described as drawing an inference, making a decision, figuring out an optimal chess move, and so on. In sum, then, physical symbol systems can be described at physical, symbolic, and semantic levels in such a way that their symbol states are instantiated in their physical states and their symbol states are semantically interpretable.5
This understanding of the human cognitive system implies a particular paradigm for the explanation of cognitive abilities. According to this paradigm, a theory of how some physical symbol system possesses a certain ability begins by specifying those input and output states of the system which are such that a system possesses that particular ability just in case it gives those outputs under those input conditions. These input and output states will have a description at the symbol level, as well-formed expressions of some formal language, and a description at the semantic level, where these formal expressions are assigned semantic interpretations. The explanation of how/why the system produces precisely those outputs under those input conditions involves providing an algorithm which is effective for transforming the input states into the output states, and which is such that the procedures specified by the algorithm apply to those states strictly in virtue of their formal properties. Of course, given an algorithm and a set of input conditions, the algorithm will determine a sequence of states intermediate between input and output, where the states in this sequence are themselves well-formed formal expressions with semantic interpretations and are obtained either directly from the input by an application of a procedure specified by the algorithm or from some subsequent state by an application of one of those procedures. According to this paradigm of explanation, then, this symbol-level description of the input and output states of a system and an algorithm effective for transforming the former into the latter, together with semantic interpretations of all the symbol states involved in the process, constitute a computational theory of the how the system possesses that ability.6
Now, suppose that the input and output states characteristic of some intelligent capacity of a physical symbol system have been specified. A computational theory of how some system possesses this capacity would be an algorithm for producing the output(s) from the input(s). But a moment's reflection reveals that, if there exists an algorithm which is effective for doing this, then there exist indefinitely many algorithms for doing it (since, if some procedure is computable, it is computable in indefinitely many ways). Each of these algorithms would constitute a computational explanation of the possession of this capacity. The question then arises as to which of these algorithms is the one which the system actually employs. There could, of course, be no behavioral evidence for choosing one of the rival explanations over the others, since ex hypothesi all the algorithms produce the same output(s) from the same input(s) and they would, consequently, all result in the same behaviors when executed. Thus, any empirical evidence which could favor one of these rival explanations over the others would have to be indirect evidence about the states which are intermediate between input(s) and output(s). The problem then becomes: What types of evidence could provide confirmation for one of the rival theories over the others, and thus provide an empirically motivated choice among these competing theories? It is this problem which I will address in what follows.7
In surveys of the types of evidence available to cognitive scientists for (dis)confirming computational theories, Pylyshyn (1978, 1981) has claimed that the principal type of such evidence is what he calls 'relative complexity evidence'.8 In what follows I will argue the following: relative complexity evidence can (dis)confirm a computational theory only if token physicalism is false; consequently, if cognitive science is to propose theories which are empirically (dis)confirmable, it must be committed to a form of type physicalism.9
Before developing this argument, however, there are some issues which should be clarified.
First, it might be suggested that the problem which I've posed isn't a genuine problem. For the problem which I've posed is that of (empirically) determining which of an indefinite number of rival algorithms is really executed by some physical symbol system in producing its output(s) from some particular input(s). And it might be thought that all of these rival theories-cum-algorithms are functionally or logically equivalent and that, consequently, a choice among them isn't necessary, since (in some sense) they can all be considered equivalent theories. This, in fact, is the line taken by Flanagan (1984).
Flanagan poses the problem as follows. Suppose that we observed a computer giving as outputs 1, 2, 3, 4, 5, 126 for inputs 1, 2, 3, 4, 5, 6 respectively. On the basis of these observations, we might hypothesize that the computer executes the following procedure: For any input n, output (n - 1)(n - 2)(n - 3)(n - 4)(n - 5) + n. Let's call this hypothesis T1, and suppose that the predictions which T1 implies are borne out by experiment; that is, let's suppose that the computer outputs 727 for input 7 and 2528 for input 8, and so on. Flanagan asks us to suppose, however, that the computer programmer comes along and claims that the computer is really executing the following procedure, call it T2: For any input n, output (n - 1)(n - 2)(n - 3)(n - 4)(n - 5) + (2n - n). Consequently, says Flanagan, T1 is not in fact "the rule the computer uses, since the computer closes each computation with the frivolous +2n - n maneuver, not with the logically and functionally equivalent +n routine" (1984, p. 124; emphases added). Flanagan continues by saying, "if we require a true explanation to refer to empirically real, and not merely predictive, processes", then T1 does not "truly explain" the computer's behavior.
On the other hand -- at least this is my intuition -- this ... is probably too strong a requirement on explanation. For both principled and pragmatic reasons we should probably allow all functionally equivalent descriptions of a computer program compatible with the evidence to count as a bona fide explanation of the computer's behavior. (1984, p. 124; emphases added)There are a couple of things wrong with Flanagan's discussion here. In the first place, his use of 'functionally equivalent' is ambiguous. In one sense, any procedures can be described as 'functionally equivalent' which produce the same output under the same input conditions, i.e. which are input/output equivalent; and, in this sense, T1 and T2 are functionally equivalent. But such input/output equivalence, which is commonly known as weak equivalence, should be distinguished from another sense of 'functional equivalence' according to which T1 and T2 aren't functionally equivalent (see, e.g., Pylyshyn 1984). For any system which executes T1, involving the +n routine, would pass through a different sequence of states than those through which it would pass in executing T2, involving the +(2n - n) routine. Thus, since the two procedures would determine different sequences of states intermediate between input and output, they would not be equivalent with respect to those intermediate states. This sense of 'functional equivalence' is commonly known as strong equivalence, where two procedures, P1 and P2, are strongly equivalent if and only if they are weakly equivalent and, for any system which can execute both P1 and P2: (a) For every state, Si, intermediate between input and output that the system occupies in executing P1, there is exactly one corresponding state, f(Si), the system would occupy in executing P2, and (b) if the system would go from state S1 to state S2 in executing P1, it would go from f(S1) to f(S2) in executing P2. Clearly, in this sense of 'functional equivalence', T1 and T2 are not functionally equivalent.
The relevance of this distinction to the problem at hand is as follows: All of the indefinitely many competing computational theories for explaining the possession of some intelligent capacity are weakly equivalent simply in virtue of the fact that they are explanations of the same cognitive capacity. Nonetheless, if that cognitive capacity is amenable to computational explanation (i.e. if it can be claimed that the system is executing some algorithm), then it is not just that there are indefinitely many weakly equivalent theories which would explain that capacity, but that there are indefinitely many weakly equivalent theories, which are also strongly inequivalent, which would explain that capacity. And each of these theories would hypothesize different sequences of (syntactically individuated) states intermediate between input and output, insofar as the algorithms to which these theories make reference would determine different sequences of such states in their execution. It thus becomes pertinent to inquire as to which state(s) the system occupies in the process of producing its output(s) for some given input(s). And it is at this point that the problem arises: How do we (empirically) determine which theory is the true description of the system's functioning?
But this seems to be precisely the problem which Flanagan doesn't think requires a solution. For Flanagan says that it is "too strong a requirement on explanation" to "require a true explanation to refer to empirically real, and not merely predictive, processes"(1984, p. 124). Thus, he seems to be saying that we should accept both T1 and T2 as "bona fide" explanations. If he means by this that both accounts are explanations (questions about confirmability aside), then I have no objection. But, in this weak sense of 'explanation', Ptolemaic astronomy explained planetary retrogression. This doesn't mean, however, that astronomers should accept both Ptolemaic and Copernican theories as truly explanatory. And, if Flanagan means that, as scientists attempting to understand the functioning of his hypothetical computer, we should accept both T1 and T2 as truly explanatory, then surely that runs contrary to scientific good sense; for these accounts offer incompatible hypotheses about the intermediate states the computer occupies. But this does seem to be precisely what he is claiming.
I think, though, that Flanagan's claim derives from his confused use of 'logically equivalent' to describe T1 and T2; and I think that this description stems from a mistaken view about the function of T1 and T2 in discussing the workings of the computer. If one were to look at these procedures simply as algorithms for solving a set of problems (such as, solve for n = 1, n = 2, and so on), then one might be tempted to describe them as 'logically equivalent' since T1 yields a correct solution if and only if T2 does. But this isn't the function which T1 and T2 are serving; for, in this context, they are hypotheses about (as Flanagan himself says) "the underlying functional structure of the computer's transformational procedures" (1984, p. 124). And, qua hypotheses, they are logically equivalent if and only if they have the same truth conditions. But they don't. T1, involving the +n routine, is true of the computer's functional structure just in case it goes through a certain sequence of states in producing its output; and T2, involving the +(2n - n) routine, is true of the computer's functional structure just in case it goes through a different sequence of states. And, again, which sequence of states it goes through determines which hypothesis is true of its functional structure. So, T1 and T2 simply aren't, contrary to Flanagan's claim, logically equivalent.
There is, perhaps, a different source of the temptation to describe T1 and T2 as 'logically equivalent'. For one might be tempted to say that there are always indefinitely many ways of formalizing the relations among the phenomena in some scientific domain -- indefinitely many ways of assigning (numerical) values to certain states (or properties) and indefinitely many functions which would describe the state transitions of some system whose states have those values assigned to them. And, one might be tempted to say, these different formalizations don't necessarily represent truly distinct understandings of the underlying phenomena, but rather may be merely notational variants of the same theory. To be tempted to say this with respect to computational theories, however, misses what is essential to them. For the symbol states and symbol transformations which appear in the formulation of a computational theory aren't simply formal representations of a process which itself isn't formal. Rather, according to the physical symbol system hypothesis, the underlying process which is described by a computational theory is itself a sequence of symbol states and rule-governed transformations of those symbols. Thus, at least with respect to computational theories, distinct formal algorithms represent distinct processes (provided, of course, the distinct algorithms aren't strongly equivalent); and this is so because computational theories are essentially syntactic, so that syntactic differences among computational theories entail genuine explanatory differences among them.
The point of this discussion has been to clarify the nature of the problem and to indicate that it can't be quickly dismissed. To state the problem again succinctly in light of the distinction between weak and strong equivalence: How can a choice among (indefinitely many) weakly equivalent, but strongly inequivalent, computational theories be empirically motivated? If we now refer to the class of weakly equivalent, but strongly inequivalent, computational theories as 'competing theories', this is just to ask: How does confirmation accrue to one of a number of (indefinitely many) competing computational theories?
But, before moving on to the real task at hand, there is a second issue requiring comment which concerns the role of simplicity in theory choice. It is something of a commonplace of scientific methodology (if not scientific method itself) that, other things (relatively) equal, the simpler among competing theories is (to be) preferred over its competitors. This idea might be taken to apply to the current problem as follows: One computational theory could be considered simpler than another if it involved an algorithm which constituted a more elegant procedure for transforming input(s) into output(s), requiring fewer intermediate steps, than the algorithm involved in the other theory. (In this way, T1 above constitutes a simpler theory than T2, since the algorithm with the +n routine is more elegant than that involving the +(2n - n) routine.) Or one computational theory could be considered simpler than another if the latter involved an algorithm which was virtually identical with the algorithm of the former theory, with the exception of determining some ineffective steps in transforming input(s) into output(s); that is, suppose that the latter requires intermediate steps in addition to the former, where these steps aren't actually effective for producing the output(s) and which are such that if they were omitted from the algorithm any system executing that algorithm would still be effective in producing the output(s). (In this way, T1 above doesn't constitute a simpler theory than T2, since the steps required by the +(2n - n) routine actually are effective for producing the output and couldn't be omitted without resulting in a procedure which is no longer effective for producing the appropriate output(s).)
Now, one might say that, if all the empirical evidence fails to motivate a choice among competing computational theories (as I will argue that it does if token physicalism is true), then the simpler among them (by the above definitions) is to be preferred over the others.
I'm somewhat sympathetic with this approach to the problem, but I think that it isn't anywhere near a solution, since it masks an assumption which is empirically improbable: that the brain makes use only of efficient computational procedures. A study by Sternberg (1966) on memory retrieval processes provides interesting evidence that the brain is in fact somewhat inefficient. In Sternberg's study, subjects were presented with lists of between one and six digits for 1.2 seconds. Two seconds later, the subjects were presented with a single digit and asked whether it had been on the list. Since reaction times increased proportionately with the length of the presented list, the hypothesis that subjects could simultaneously 'see' all the entries on the list in memory could be ruled out; subjects were scanning the lists. The most efficient scanning process under these conditions, of course, would be a 'terminating search', where the subject discontinues the search as soon as they come across the target digit in the memorized list. But, Sternberg's experiments showed that reaction times didn't vary as a function of the position of the target digit in the list; they were independent of the position of the target digit. And this seems to imply that retrieval processes involve 'exhaustive searches', where subjects scan the entire list before determining whether the target digit is on it. Thus, at a very primitive level of cognition the brain is not maximally efficient. And, if the brain is inefficient at very basic levels of cognition, its inefficiency should be expected to increase proportionately with the complexity of the tasks to which it is applied (and the complexity of the procedures involved in accomplishing those tasks). That is, if the brain isn't maximally efficient with processes like memory retrieval and storage and other such primitive processes, then elaborate computational procedures which exploit these primitive capacities should exhibit an even greater degree of inefficiency, since the inefficiency of the primitive processes would be compounded when such processes are combined in more complex procedures.
The upshot is that computational theories of human cognition involving inefficient procedures shouldn't be ruled out a priori. And this implies that one computational theory shouldn't be preferred over another on grounds of 'simplicity' alone, if by the 'simpler' theory we mean that theory which involves more efficient or elegant computational procedures. If we are to prefer one computational theory over another, it must be for strictly empirical reasons and not for any such a priori reasons.
Third, I want to make explicit an assumption which I will be deploying in the arguments to follow. I will be assuming that a bit of empirical data is relevant evidence with respect to a choice among competing theories only if that bit of data provides grounds for preferring at least one of the competing theories over at least one of the others.10 The notion of relevant evidence with which I'm working, here, is somewhat different from Glymour's (1980). Glymour takes the relevance relation to be a relation between a bit of evidence and a theory. Thus, as Glymour develops the notion, a bit of evidence is relevant to some theory, in deductivist terms, just in case a description of that evidence is deducible from the theory together with auxiliary hypotheses; a bit of evidence is relevant to some theory, in Bayesian terms, just in case the posterior probability of that theory is greater than its prior probability; and a bit of evidence is relevant to some theory, in bootstrapping terms, just in case an instance of a hypothesis in that theory can be deduced from a description of that bit of evidence together with other hypotheses in the theory. But, according to this conception of evidential relevance, it is conceivable that a bit of empirical data would be relevant to absolutely every one of a number of competing theories (indeed, relevant to every possible competing theory). My intuition, however, is that in such a case that bit of data is not really relevant to any of the competing theories. This is because I think that the concept of relevant evidence is best understood in a context of theory choice and not in a context where confirmation is viewed as a relation between a body of data and a theory considered in isolation from any of its (possible) competitors. Thus, even though I have no argument for this, in what follows I will assume that a bit of data is relevant evidence with respect to some theory only if that bit of data is relevant to a choice between that theory and its competitors (in the sense defined above). Put simply, I will assume that a bit of data is relevant evidence with respect to a choice among competing theories only if that data discriminates among the competitors.11
I can now state the thesis of this essay a little more clearly and succinctly. I will argue that, if token physicalism is true, none of what Pylyshyn calls 'relative complexity evidence' is relevant to any computational theory of some cognitive process (since, if token physicalism is true, relative complexity evidence cannot be relevant to a choice among competing computational theories). I will attempt to show, however, that, if some form of type physicalism is true, relative complexity evidence is relevant to computational theories. If these arguments are successful, I take their significance to be as follows: Type physicalism is the only metaphysical theory about the relation between the states postulated by theories in the special sciences and the states postulated by the more basic (physical) sciences which is compatible with the use of relative complexity evidence to (dis)confirm computational theories of cognition. In addition, relative complexity evidence is in fact used by cognitive scientists to (dis)confirm computational theories. Consequently, since I will assume that metaphysical views regarding physicalism should be conditioned by actual scientific practice, there are strong methodological reasons for accepting type physicalism.
Finally, before turning to the actual arguments, let me say something about the distinction between token physicalism and type physicalism and the role that it will play in the arguments to follow.
In their general form, type physicalism and token physicalism are doctrines about the relation between the states over which the laws of special sciences generalize and the states over which the laws of physics generalize (see Fodor 1981).12 But these doctrines are also taken to have specific implications with respect to the relation between computational theories of cognition and neuroscientific theories of the brain processes in which these computational procedures are realized; and only these specific implications concern me here.13 Both doctrines hold that every state referred to by some computational theory has, in addition to its description as a symbol structure, a description in the vocabulary of neuroscience. In other words, both doctrines hold that every state over which computational theories generalize is a brain state.14 They differ, however, in how they construe the relations between the computational taxonomy of states and the neurological taxonomy of states.
According to type physicalism, there is an isomorphism between the computational taxonomy and the neurological taxonomy such that every type of state in the taxonomy of a computational theory corresponds to some type of state in the neurological taxonomy.15 This implies that whenever some individual state is describable as an instance of some type of computational state, say C, it is also describable as an instance of some single type of neurological state, say N, such that that individual state cannot be described as an instance of C without also being describable as an instance of N. Consequently, every individual state which has a description as a state of type C also has a description as a state of type N.
Token physicalism denies that there is such an isomorphism between the taxonomy of a computational theory and the taxonomy of neuroscience. Thus, according to token physicalism, while every individual state which is describable as a state of type C also has a description as an instance of some neurological state type, two individual states describable as instances of C could be such that one is describable as an instance of N while the other is describable as an instance of some neurological state type other than N. Indeed, according to token physicalism, it would be possible for the set of individual states which are describable as instances of type C to be such that no two of its members are describable as instances of the same neurological state type.
By way of bringing into sharper focus this distinction between type and token physicalism and its relevance to the current problem, let a computational process be represented by an ordered n-tuple of types of state in the taxonomy of some computational theory and let CP denote the n-tuple which, according to that theory, is intermediate between certain specified input(s) and output(s). Further, let a neurological process be represented by an ordered n-tuple of types of state in the taxonomy of neuroscience and let NP1, NP2, ... NPn denote distinct n-tuples. According to type physicalism, whenever some system undergoes CP, that system undergoes a specific type of neurological process, say NP1; that is, according to type physicalism, on every occasion the system undergoes CP it undergoes NP1. And this fact can be expressed by saying that NP1 realizes or instantiates CP. Token physicalism denies this. According to token physicalism, one occasion on which some system undergoes CP can be an occasion on which it undergoes NP1, while some other occasion on which it undergoes CP can be an occasion on which it undergoes NP2. Indeed, according to token physicalism, there need be no two occasions on which some system undergoes CP while undergoing the same neurological process. And this fact can be expressed by saying that CP can be realized or instantiated by numerous distinct neurological processes.
Token physicalism, however, doesn't allow for the possibility that CP would be realized by just any arbitrary n-tuple of neurological states. There is one restriction which token physicalism places on the realization of computational processes, which I will call the causality constraint. To see this, let <Ci,Ck> be any contiguous pair of states in the n-tuple CP; as such, Ck would be a state which, according to the relevant computational theory, follows from Ci in virtue of some (primitive) transformational procedure specified by the theory. The causality constraint which token physicalism places on the realization of CP is as follows: no pair of individual, spatiotemporally contiguous brain states, say <b1,b2>, can be token realizations of <Ci,Ck> unless those brain states are causally related under their neurological descriptions, i.e. unless the pair of brain states <b1,b2> is subsumable under some causal law of neuroscience.
With these preliminaries out of the way, I can state even more precisely than before the claim for which I will argue. I will argue that relative complexity evidence cannot be relevant to a choice among competing computational theories if the only restriction on the physical realization of the processes hypothesized by those theories is the minimal causality constraint required by token physicalism. Only if there are type physicalist constraints on the possible physical realization of those computational processes could relative complexity evidence be relevant to a choice among competing computational theories. (Actually, as I will argue, there must be an additional constraint as well.)
So let me now turn to the discussion of relative complexity evidence and the role which Pylyshyn sees it playing in the confirmation of computational theories.
Pylyshyn introduces his discussion of relative complexity evidence in the context of (dis)confirming computational theories of arithmetic ability. To (dis)confirm such theories, Pylyshyn says:
We could attempt to rank various arithmetic problems in order of their complexity in the model. Various complexity measures might be sought but two simple ones are the time taken to complete the task and the number of elementary operations (e.g., machine cycles) which they required....The idea behind relative complexity evidence is that arithmetic problems exhibit varying degrees of difficulty or, as Pylyshyn says, 'complexity'. So, the strategy is to rank order problems with respect to their difficulty when solved by human subjects and also to rank order them with respect to their difficulty according to the procedure of the competing computational theories of human arithmetic ability. Once this is done, these rankings can be compared. And, if the ranking of problems with respect to their difficulty according to the procedure of one of the competing theories differs from the ranking of the same problems derived from the study of human subjects, that theory is disconfirmed; if the rankings are the same, the theory is confirmed.
We can now do the same for human subjects. The scale of complexity here can depend on such measurements as the time taken to complete the task or the frequency of errors. (1978, p. 98)
Pylyshyn mentions three measures by which the degree of difficulty of problems can be determined: a measure of the processing time, i.e. the time taken to solve some problem, the number of elementary steps involved in solving it, and the frequency with which errors are made in attempting to solve it. Let me discuss these measures and their putative use in reverse order.
First, Pylyshyn suggests that one way of ranking problems in order of difficulty is by determining how frequently errors are made in attempting to solve them. Thus, there might be a certain class of problems which never lead human subjects to make errors when attempting their solution, another class which leads to errors only once out of every 50 attempted solutions, another which leads to errors once in every 25 attempted solutions, and so forth. This, then, provides a ranking of the problems according to their difficulty for human subjects, which could then be compared to the rankings similarly generated by the theories.
This type of evidence, however, isn't pertinent to the problem which I posed. The reason is that all the competing computational theories in the problem situation are weakly equivalent, i.e. they are all input/output equivalent. And the input/output for which they are effective procedures represents the input/output of the ability of the human subjects which is being explained. But the arithmetic ability of the human subjects isn't necessarily a disposition always to give correct answers to the problems which they're posed; more than likely, of course, they will be disposed to make certain errors. And this means that the input/output specification of their disposition will contain some outputs which aren't arithmetically correct relative to their corresponding inputs. Consequently, since ex hypothesi each of the competing computational theories is a perfect behavioral simulation of the ability of the human subjects which is being explained, each of the competing computational theories would be effective for the input/output profile of the human subjects; that is, every theory would be an effective procedure for producing certain systematic errors. Or, to put it another way, each of the competing computational theories is already weakly equivalent with whatever procedure the human cognitive system actually does employ. Ex hypothesi, then, each of the competing theories would make exactly the same errors that the human subjects make. So, none of these theories would be disconfirmed by such evidence; and, thus, no such evidence would be relevant to a choice among these competing theories.
Second, Pylyshyn suggests that problems can be ranked in order of difficulty by determining the number of elementary, intermediate steps required to solve them. Thus, by determining the number of elementary, intermediate steps required by human subjects to solve each of the problems in the target class, all of these problems can be rank ordered. This ranking can then be compared with similarly generated rankings for each of the competing theories.16
Now, certainly, if it could be shown that human subjects took, say, 10 steps to solve problem P1 and 14 to solve P2, whereas the procedure of some one of the competing theories, T, required 8 steps to solve P2 and 18 to solve P1, then T could be considered disconfirmed. But there are two problems which militate against the possibility of using this measure of difficulty to disconfirm computational theories, both of which pertain to the possibility of gathering reliable evidence about the elementary, intermediate steps involved in human cognitive processes. For according to Pylyshyn, the methods for gathering evidence about the intermediate states involved in human cognitive processes "consist mostly of the analysis of thinking-out-loud protocols, supplemented by some inferences about missing states" (1978, p. 97). In other words, the subject is given a series of tasks and is asked to 'think aloud' while completing the tasks and report the steps they are going through in the process of completing them. Protocols are these first-person reports of cognitive processes.17 But, of course, no one assumes that subjects under these conditions would be consciously aware of all the cognitive processes which were causally productive of their responses. Thus, the protocols must be, as Pylyshyn says, "supplemented by some inferences about missing states". The assumption, here, is that the protocols will provide at least a reasonably reliable guide to aspects of the total cognitive process which intervened between input and output. That is, it is assumed that the first-person reports will provide evidence as to at least some of the cognitive states intermediate between input and output. And, where there appear to be gaps in the first-person accounts, these can be filled by inferences about the most probable steps intermediate between the reported steps.
The first problem, then, with using protocols to determine how many elementary, intermediate steps human subjects take in the solution of any given problem is that there is empirical evidence that first-person 'reports' of cognitive processes are in general unreliable, since they are not based on actual introspection. In a battery of experiments in which a wide variety of cognitive phenomena were studied, Nisbett and Wilson (1977) found that subjects consistently failed to report the effects of certain stimuli in the experimental setting on the cognitive processes involved in completing tasks they were given. Cognitive phenomena which are likely candidates for computational explanation and for which Nisbett and Wilson found this result include, among other things, problem-solving processes (pp. 240-241), semantic associations (p. 243), and preference orderings (pp. 243-244). They concluded from their studies that:
People often cannot report accurately on the effects of particular stimuli on higher order, inference-based responses.... The accuracy of subjective reports is so poor as to suggest that any introspective access that may exist is not sufficient to produce generally correct or reliable reports. (p. 233)This implies that protocols from subjects regarding such cognitive processes as solving arithmetic problems, figuring out chess moves, and decision making are not reliable evidence about the actual sequence of intermediate states involved in these processes.
But, interestingly, apart from the fact that subjects in experimental settings failed to report the effects of demonstrably efficacious stimuli, Nisbett and Wilson found that subjects who read descriptions of the same experimental settings made predictions about their probable cognitive processes in those settings which were identical to the reports given by the subjects who actually participated in the original experiments (pp. 247-248). And this group of "observer" subjects clearly weren't introspecting any actual cognitive processes. Thus, Nisbett and Wilson concluded,
when people are asked to report how a particular stimulus influenced a particular response, they do so not by consulting a memory of the mediating process, but by applying or generating causal theories about the effects of that type of stimulus on that type of response. They simply make judgments, in other words, about how plausible it is that the stimulus would have influenced the response. These plausibility judgments exist prior to, or at least independently of, any actual contact with the particular stimulus embedded in a particular complex stimulus configuration. (p. 248)Consequently, cases in which first-person reports are correct are simply cases in which the causal theory with which the subject is operating just happens to be correct; they are not cases of genuine introspection (p. 233).
Now, Nisbett and Wilson's results have not gone unchallenged. One notable challenge comes from Ericsson and Simon (1980), who argue that Nisbett and Wilson's conclusions wouldn't apply to non-automatic processes, i.e. processes which involve conscious deliberation regarding, and attention to, the current task. In such cases, they argue, traces of the processes involved in completing cognitive tasks would be present in short-term memory and, consequently, subjects would be able to report such processes while they are occurring.18 In addition, however, Quattrone (1985) has argued, in an article which admits of no brief summary, that most of the experiments on which Nisbett and Wilson base their conclusions can be reinterpreted so as not to pose too serious a challenge to the idea that subjects can make reliable reports about their own cognitive processes.
But, even if these criticisms of the Nisbett and Wilson research are right (and, I think, the evidence isn't conclusive), there still remains a second serious obstacle to determining the number of elementary, intermediate steps involved in human cognitive processes. For the steps about which evidence must be gathered are the elementary steps involved in the computational processes which constitute human cognition. So, even if it were granted that human subjects have introspective access to cognitive processes (i.e. that the reports which they do make are in fact reliable), it wouldn't thereby follow that they have access to the elementary steps involved in those processes. Indeed, even if it were plausible to think that certain intermediate steps in human computational processes left traces in short-term memory, it would be quite implausible to suppose that every primitive transformation of the symbol structures involved in the process would be accessible to introspection. For suppose that some subject solving a logic problem gives a report something like this: "First I noticed that I could apply modus ponens to lines 1 and 3 and then I saw that I could apply DeMorgan to the result to get the desired formula." Even if we grant that these reports are accurate, noticing that modus ponens applies and seeing that DeMorgan applies are surely not elementary steps of the cognitive processes involved; they would be the results of more fine-grained processes below the level of the subject's awareness. And there would be numerous strongly inequivalent transformational procedures, each involving a different number of elementary steps, which could yield these results. Consequently, this sort of report does not actually give evidence as to the number of elementary computational steps involved in the cognitive process. Thus, without such evidence as to how many elementary, intermediate steps human subjects take to solve any given problem, it would never be possible to generate a ranking of problems as a function of the number of elementary, intermediate steps involved in their solutions.
Now, of course, one might respond that protocols aren't necessarily the only type of evidence which we could have to determine the number of elementary steps taken by human subjects in the solution of some problem. One could claim that the time taken to solve some problem could be evidence for the number of elementary steps involved.19 That is, one could claim that, if it takes a human subject longer to solve P2 than to solve P1, P2 must involve a greater number of elementary steps than does P1. But, to respond in this way is just to reduce all relative complexity evidence to the use of processing time measures. For there is no distinction between ranking problems in order of the time that it takes human subjects to solve them and ranking those same problems in order of the putative number of elementary steps required to solve them, where the number of elementary steps required is directly inferred from the time taken to solve them. So, since processing times appear to be the only potentially useful measure of the degree of difficulty of a problem for human subjects, let me turn now to a discussion of this type of evidence.
Pylyshyn suggests that the time it takes to solve problems could generate a ranking of problems from those which require the most time to solve to those which require the least time. And, again, any theory which generates an ordering which differs from that generated by the processing times of human subjects would be disconfirmed, while those which generate the same ranking would be confirmed.
The first thing to note about Pylyshyn's recommended procedure, here, is that computational theories are abstract descriptions of the functioning of physical symbol systems, not physical symbol systems themselves. Second, processing times are measures of the functioning of physical systems; that is, a processing time is a measure of the duration of a physical process. Thus, it can't be determined how long it takes to solve some particular problem according to the procedure hypothesized by some computational theory simply by looking at that theory's computational description of the solution (i.e. its symbol-level description of the steps involved in the solution). For how long it takes to solve some particular problem by some computational procedure depends on the way that procedure is realized in some particular physical system. The same procedure could take some time t to solve a particular problem in one physical system and take some time greater than t in a different physical system. Consequently, without information about how a computational procedure is physically realized, it is impossible to determine how much time it might take, by that procedure, to solve any given problem. In the absence of such information, then, it is impossible to use processing time measures to rank problems in order of their difficulty for any of the competing computational theories.
Thus, if relative complexity evidence is to be used to empirically motivate a choice among competing computational theories, the ranking of problems in order of complexity in the computational theories must be based on the number of elementary, intermediate steps involved in their solution, and the ranking of those problems in order of complexity for human subjects must be based on the processing times of those human subjects. For we have seen that the number of elementary, intermediate steps for human subjects can't be determined; and we have seen that the processing times for computational theories can't be determined. Consequently, the way in which relative complexity evidence must be used is as follows. Rank order problems for each of the competing computational theories in terms of the number of elementary, intermediate steps involved in the solution of those problems, then rank order those problems in terms of the time which it takes human subjects to solve them. Once this is done, these rankings can be compared as before.
But note that this use of relative complexity evidence can (dis)confirm one or more of a group of competing computational theories only if it is supposed that these two types of ranking are commensurate. If there is no reason for thinking that they are commensurate, relative complexity evidence cannot be relevant to a choice among such theories. What I will now argue is that, if token physicalism is true, there is in fact no reason to suppose that these rankings would be commensurate; consequently, relative complexity evidence could not (dis)confirm any of the competing computational theories. But, if type physicalism is true, the supposition that these rankings are commensurate can be justified; consequently, relative complexity evidence can be relevant to a choice among competing computational theories only if type physicalism is true.
To see this, consider the following simplified situation. Let P1 and P2 be problems and T1 and T2 competing computational theories. And suppose that T1 hypothesizes that P1 requires a greater number of elementary, intermediate steps than P2 (but that all the steps involved in solving P2 are involved in solving P1), while T2 hypothesizes that P2 requires a greater number than P1(but that all the steps involved in solving P1 are involved in solving P2). Suppose further that processing time studies of human subjects yield the result that P1 takes more time to solve than P2.
First let me show that, if token physicalism is supposed true, this evidence could not be relevant to a choice between T1 and T2. Then I will show that, if type physicalism is supposed true, this evidence would be relevant.
The first problem, if we suppose that token physicalism is true, is that token physicalism requires only that the intermediate states in a computational process be realized by some brain states or other (as long as the causality constraint is satisfied). This is compatible with a wide range of possibilities. For example, a sequence of computational states could be realized by a sequence of intraneuronal states, by a sequence of firing neurons, or by a sequence of states of neuronal ensembles. Thus, a sequence of n computational states would have shorter duration if realized by a sequence of intraneuronal states than if realized by a sequence of firing neurons, and this latter would have shorter duration than if those computational states were realized by a sequence of states of neuronal ensembles. And since, if token physicalism is true, we could never really know what brain process realizes a computational process, the above evidence could neither confirm T1 nor disconfirm T2. The reason is simply that T2 could explain the human processing time data as easily as T1, simply by hypothesizing that the steps involved in solving P2, while greater in number than those involved in solving P1, were realized in a 'faster' brain process than that which realized the steps involved in solving P1. Consequently, if token physicalism is true, the above evidence could not motivate a choice between T1 and T2.
Now, of course, the natural solution to this problem is to claim that not all brain states are computationally relevant, i.e. that not all brain states are realizations of symbol structures. Thus, it could be claimed that intraneuronal states, for example, are not computationally relevant and, consequently, are not plausible candidates for the realization of computational processes. So, if the firing of a neuron, say, is taken as the physical realization of an elementary computational step, then it can be claimed that, since human processing times indicate that P1 takes more time to solve than P2, P1 must involve a greater number of neuron firings than P2 and, hence, a greater number of elementary computational steps. Therefore, it could be argued, T1 is confirmed by this evidence, whereas T2 is disconfirmed.
There are, however, a couple of problems with this proposed solution. One problem is that, if token physicalism is true, it is strictly ad hoc. For, if token physicalism is true, it follows that we could never discover, simply by studying the brain, what computational processes are involved in human cognition. This is because token physicalism allows the possibility that tokens of distinct brain state types could realize the same type of computational state and that distinct tokens of the same type of brain state could realize distinct types of computational state. And this entails that we could never discover, simply by studying the brain, that, or even whether, some particular brain state performs some particular computational function. Thus, if token physicalism is true, we could never be empirically justified in assuming that the firing of a neuron, say, is the physical realization of an elementary computational function. Such a solution to the above problem would be purely stipulative.
Even if we waive this objection, however, and allow that elementary computational steps are realized by the firings of neurons, there remains a second difficulty. For the firing time of a neuron varies between 0.2 and 0.5 msecs., depending on the type of neuron (Churchland 1986, p. 58). So, even if it is assumed, based on the human processing time data, that P1 involves a greater number of elementary computational steps (i.e. neuron firings) than P2, it is still possible, if token physicalism is true, that the steps involved in solving P1 are realized in a 'faster' sequence of neuron firings than the steps involved in solving P2. Consequently, T2 could still provide as adequate an explanation of the human processing time data as could T1; and, hence, such data could neither confirm T1 nor disconfirm T2.20
There is, however, another way of responding to these arguments. One could argue that the foregoing considerations are plausible only if the human processing time data is derived from single measurements or from some very small number of measurements. The reasoning, here, would go as follows. If the processing time data is derived from a single measurement of how long it takes some particular subject, S, to solve P1 and a single measurement of how long it takes S to solve P2, then this data indeed would not provide much evidence for T1, since T2 could explain the data in the way just discussed. In other words, in such a case, it might be plausible to think that it just so happened that on these occasions the process involved in solving P1 was realized in a 'faster' brain process than the process involved in solving P2. But if we take repeated measurements of S's processing times and find that on each occasion the solution of P1 takes longer than the solution of P2, it becomes less probable that it just so happened that on every one of those occasions the process involved in solving P1 was realized in a 'faster' brain process than that of P2. Further, if we take measurements from a battery of other subjects and find the same uniformity, T2's explanation of the data would then be rather improbable, since the probability that not a single one of the solutions of P1 would be realized in a 'slower' brain process than that of P2 would be very low. Consequently, one might argue, if the data were in fact as supposed, it would confirm T1 and disconfirm T2; and, hence, the above discussion about token physicalism is a red herring.
Now, I think there is a kernel of truth in this argument; for I think the interpretation of the data required to support T2 would be rather improbable. But I don't think the discussion about token physicalism is a red herring. For the important question at this point becomes: What justifies the judgment that the interpretation of the data required to support T2 would be improbable? Of course what justifies it is the supposition that there must be some reason why the processing time data exhibits the uniformity it does. And, if T2 'explains' this uniformity by some just-so story, then that putative explanation is less satisfying than one which appeals to some principled reason why the processing time data exhibits such uniformity. But note that, if token physicalism is true, there could be no principled reason why the processing time data exhibits this uniformity. If token physicalism were true, there would be no reason whatsoever to expect any sort of uniformity among processing time data; that is, since token occurrences of some type of computational process could be realized in token occurrences of different types of neurological process, which differ in their duration, there would be no reason whatsoever to expect each of those token occurrences of that type of computational process to exhibit the same duration. In particular, there would be no reason to expect that the solution of P1 would always take human subjects longer than the solution of P2. If the data indicated this sort of uniformity, it would be purely accidental if token physicalism were true. Thus, if it is supposed that there must be some principled explanation of the uniformity among processing time data, the grounds for this supposition can't derive from a commitment to token physicalism.
Based on these considerations, I think it's safe to conclude that, if it is supposed that token physicalism is true, relative complexity evidence would never be relevant to a choice among competing computational theories. Indeed, what I think the foregoing shows is that, if relative complexity evidence is to be relevant to a choice among competing computational theories, there must be some way of providing adequate grounds for postulating the commensurability of complexity measures derived from human processing times and those derived from counting the number of elementary, intermediate steps in a process hypothesized by a computational model. And token physicalism can't provide these grounds. But, if we suppose that type physicalism is true -- if we suppose that every type of computational state corresponds to some type of brain state -- , we have a solution to the problem which confronted the use of relative complexity measures under the supposition that token physicalism is true. To see this, let's consider the same simple situation described above regarding the rankings of the problems P1 and P2 according to the theories T1 and T2.
If we now suppose that type physicalism is true, it would indeed follow that, according to T1, the solution of P1 would require more time than the solution of P2 and that, according to T2, the solution of P2 would require more time than the solution of P1. For consider T1, which hypothesizes that P2 requires, say, n steps. If type physicalism is true, then each type of computational state in the process of solving P2 corresponds to some type of brain state. And, since P1 involves each of those n steps and others in addition, whenever some system solves P1, it undergoes exactly the same type of brain process which it undergoes when solving P2 and then some additional states as well. Thus, if type physicalism is true, T1 would require that P1 take more time than P2. And similar points hold, mutatis mutandis, for T2. Thus, it would appear that the human processing time data, according to which it takes more time to solve P1 than to solve P2, confirms T1 and disconfirms T2 -- if, that is, we suppose that type physicalism is true.
But this solution to the problem of justifying the commensurability of the two types of relative complexity measure only works if we suppose, as we did, that the solutions of the problems, according to all the competing theories, involve the same sequence of steps with the exception that one solution involves additional steps. Consequently, if we don't assume that the solution of P1, according to T1, involves the same steps that are involved in the solution of P2 and then some (and vice versa, in the case of T2), relative complexity evidence is still irrelevant to the choice between T1 and T2. For suppose that T1 still hypothesizes that P1 requires more steps than P2, and that T2 still hypothesizes that P2 requires more steps than P1, but that now according to both theories P1 and P2 involve entirely distinct computational sequences. Even if we suppose that the human processing time data is the same as before (P1 taking longer than P2), T2 can still provide as adequate an explanation of this data as T1. For now T2 could explain the data by postulating that the computational process involved in solving P2 is realized in a 'faster' sequence of types of neuron firings than the sequence of types of neuron firings which realize P1. Were this the case, the solution of P2 would take less time than that of P1 even if it did involve more elementary, intermediate steps (provided, of course, that the difference between the number of steps involved in each solution wasn't too great).
Clearly, then, in order for relative complexity evidence to have general relevance to a choice among competing computational theories, not only must it be supposed that type physicalism is true, but the following condition must be satisfied as well: T1 and T2 must each be accompanied by an actual assignment of brain-state types to the computational-state types which they postulate. This would provide for the possibility of associating a sequence of determinate brain states with each sequence of computational states postulated by each theory. If we suppose again, for the sake of simplification, that the brain-state types which are assigned to computational-state types in this way are neuron firings, then the known firing times for each of the types of neuron involved in the assignment could be used to calculate a duration for the sequence of those neuron firings. This in turn would allow associating some estimated processing time with each sequence of computational states. With this condition satisfied, T1 and T2 would no longer imply just that the solution of one of the problems would take longer than the other, they would imply reasonable estimates of the specific processing time each solution would involve. And with such estimates made prior to the gathering of data regarding human processing times, there would be greater likelihood of conflict between the data and the estimates made by competing theories; hence, there would be greater likelihood that the data would disconfirm at least one of the competing theories.
Satisfying this condition, however, would not in itself guarantee the general relevance of relative complexity evidence to computational theories. For after the human processing time data is gathered, ad hoc modifications could always be made in the brain-state type/computational-state type assignments of a theory in order to accommodate the data. So, if the human processing time data turned out to be close to the processing times estimated by T1 and rather different than those estimated by T2, a new assignment of brain-state types to computational-state types could be concocted for T2 which would bring its processing-time estimates into accordance with the data and, hence, enable T2 to provide as adequate an explanation of the data as T1.
There would, however, be two problems with this way of attempting to protect T2 from disconfirmation. First, even though ad hoc modifications aren't always bad, if the data clearly favors one of a number of competing theories prior to the ad hoc modification of one of its competitors (as in the situation just described), then that is certainly a strong reason for preferring that theory which didn't require ad hoc modification in order to account for the data. Second, not just any ad hoc modification would be admissible. The sequence of brain-state types assigned to some computational process must be a neurologically possible sequence, in the sense that each contiguous pair of brain-state types in the sequence must be subsumable under some neurological law. (In this way, brain-state type/computational-state type assignments must satisfy a constraint similar to, but somewhat stronger than, the causality constraint of token physicalism.) And this, in itself, would seriously constrain the possible ad hoc modifications available to protect a theory from disconfirmation.
The existence of these two problems with ad hoc modifications of competing computational theories would radically temper the force of such modifications. Thus, the condition requiring each of the competing theories to be accompanied by an actual brain-state type/computational-state type assignment would provide adequate rationale for considering relative complexity evidence generally relevant to computational theories.
But consider what must be the case for this condition to be satisfied. The development of computational theories of cognition must be conducted concurrently with research into the neurophysiology of the brain, since only in this way would it be possible to provide the brain-state type/computational-state type assignments necessary to make relative complexity evidence relevant to a choice among competing computational theories. This model of research into the computational procedures constitutive of cognition is what Churchland (1986, pp. 362-376) calls the co-evolutionary research ideology and it stands in sharp contrast to the research paradigm which typically accompanies a commitment to token physicalism.21 For it is commonly assumed, by those who are committed to token physicalism, that the construction and confirmation of computational theories of human cognition can be undertaken independently of, and regardless of, neuroscience. This is brought out most clearly in what Pylyshyn calls the 'proprietary vocabulary hypothesis': the idea that the theoretical vocabulary of cognitive science is entirely distinct from the vocabulary of neuroscience and that questions about the nature of the computational procedures (or algorithms) involved in human cognition "can be answered without appealing to the material embodiment of the algorithm" (1980, p. 116). Thus, as Pylyshyn says, "the exact nature of the device that instantiates the process is no more a direct concern to the task of discovering and explaining cognitive regularities than it is in computation [in standard computing systems]" (1980, p. 114; emphasis added). This is also the attitude characteristic of Simon (1985) and others who take the programs of artificial intelligence systems, which are constructed strictly with an eye to the symbol and semantic levels, to be legitimate theories of human cognition. When put into practice, this idea means that cognitive scientists can arrive at an understanding of the computational procedures which are characteristic of human cognition without worrying about how such procedures are realized in the brain. Facts about the structure and function of the brain, on this view, are essentially irrelevant to determining which computational procedures are involved in human cognition.
But, if the arguments of this essay are right, then it's simply not true that it can be determined what computational procedures are involved in human cognition independently of the question as to how those procedures might be realized in the brain. For determining what those computational procedures are involves not simply hypothesizing that such-and-such are the computational procedures, but confirming that hypothesis as well. As we have seen, however, for any computational theory, there are (theoretically) indefinitely many competitors, i.e. weakly equivalent but strongly inequivalent theories; and relative complexity evidence can be relevant to a choice among these competing theories only if they are accompanied by brain-state type/computational-state type assignments (which, in turn, can be accomplished only if it is supposed that token physicalism is false). And that is just to say that competing computational theories can be (dis)confirmed by relative complexity evidence only if they are accompanied by hypotheses about how the procedures which they postulate are realized in the brain.22
Of course, at this point, one might be tempted to suggest that cognitive scientists might simply use other types of evidence to (dis)confirm computational theories, and that the use of these other types of evidence might not require the supposition that type physicalism is true. And Pylyshyn does, in fact, discuss two other types of evidence available to cognitive scientists to (dis)confirm computational theories. The first of these is intermediate state evidence, which simply involves the use of protocols (1978, p. 97). But we have already seen the problems with the use of protocols in connection with relative complexity evidence; and these problems would still plague protocols if they were used as a general means for choosing among competing computational theories. The second is component analysis evidence (1978, p. 98). The idea behind component analysis evidence is that a good theory of human cognitive processes is one which simulates not only the performance of some overall task, but the performance of all the subtasks which are involved in completing that overall task as well. Thus, the procedures of the competing computational theories should be compared with the performance of human subjects not only with respect to the overall task, but with respect to these subtasks also. But, Pylyshyn suggests, the methods used in these comparisons are protocols and relative complexity evidence. The only difference, here, is that the data from protocols and relative complexity evidence are being gathered with respect to these subroutines. Naturally, however, since component analysis evidence essentially involves the use of protocols and relative complexity evidence, any problems with these types of evidence will be problems with component analysis evidence as well. And we have seen, first, that the Nisbett and Wilson research provides general grounds for skepticism regarding the accuracy of protocols and, second, that, even if they are reliable, their reliability extends only to very high-level features of cognitive processes which could be accounted for by numerous strongly inequivalent lower-level computational procedures. Consequently, since the evidence from protocols is too severely limited to be of any real value, and since component analysis evidence isn't genuinely distinct from relative complexity evidence, relative complexity evidence represents the only usable form of evidence.
Now, by way of concluding, let me comment on the overall significance of the arguments I've presented.
I take these arguments to show that cognitive science must be committed to type physicalism if it is to be in the business of proposing computational theories of cognition which can be empirically confirmed over (potential) competing theories. But I don't take these arguments to show anything more than this. So, the moral of these arguments could be taken to be that cognitive science, if it is to be scientific, should not be in the business of proposing computational theories of cognition. Or, it could be taken to be that cognitive science, qua science, is impossible, since it is in the business of proposing theories which are such that a choice among them and their (potential) competitors cannot be empirically motivated. Both these ways of reading the moral of the foregoing arguments, however, presuppose the truth of token physicalism; and neither of them are the reading which I prefer. Rather, the moral I prefer to extract is as follows: Cognitive scientists do in fact sometimes propose computational theories of cognition, they do in fact sometimes appeal to relative complexity evidence to support those theories, and type physicalism is the only metaphysical view of the relation between computational states and brain states which is compatible with this use of relative complexity evidence; consequently, since type physicalism is the (implicit) metaphysical commitment of a working science, this in itself is prima facie evidence for thinking that type physicalism is true.
This way of reading
the moral of the foregoing arguments would imply, then, that the debate
between type physicalists and token physicalists should be taken out of
a metaphysical context and placed in a methodological context. And
this implies that the real issues about the distinction between type physicalism
and token physicalism don't pertain to what may or may not be true of doppelgangers
in neighboring possible worlds, Martians, or mad persons. Rather the real
issues pertain to what is logically required by the actual practice of
working cognitive scientists. And I believe that the foregoing arguments
provide reason for thinking that, with respect to cognitive scientific
practice, type physicalism is to be preferred to token physicalism.23
1. See, e.g., Dennett (1971), P. S. Churchland (1986), and Pylyshyn (1984). [return to text]
2. I say that 'at least some of' their state transitions can be subsumed under natural law, since it is possible that some of their state transitions as described at the symbol level aren't subsumable under natural law. [return to text]
3. I say that 'at least some of' their physical states instantiate symbol tokens, since it is possible that there are physical states of the system which are computationally irrelevant, i.e. states which don't instantiate symbol tokens and which have no effect on the state transitions of the system as described at the symbol level. [return to text]
4. I say that relations among 'at least some of' their symbol states are isomorphic to semantic relations among sentences of some language, since it is possible that there are certain symbol states of the system to which no semantic interpretations are assigned. Such states would be computationally relevant, i.e. they would be implicated in state transitions at the symbol level, but they would not directly result in any changes in the system as described at the semantic level. [return to text]
5. This description is limited, of course, to what Haugeland (1985) has called 'Good Old-Fashioned Artificial Intelligence' (or GOFAI) and doesn't encompass newer parallel distributed processing (PDP) or connectionist theories of cognition. I will confine my discussion in this essay to the GOFAI conception of the human cognitive system for two reasons. First, I am not yet entirely clear about the full implications of my arguments with respect to PDP models. Second, the flurry of PDP work being done at the moment hasn't won over everyone in the field; there are still those who subscribe to the GOFAI conception (notably Fodor and Pylyshyn) and the arguments of this essay are directed at them. (For further comments on PDP models, see notes 20 and 22.) [return to text]
6. There are a few detractors from the view of cognitive scientific explanation which I've just sketched. For example, Stich (1983) and P. S. Churchland (1986) have argued that the best computational theories we will come up with will be purely formal, symbol-level descriptions of the cognitive system, such that they won't be isomorphic to semantic relations among sentences of a natural language and, consequently, won't be semantically interpretable by sentences of a natural language. This issue, however, will be unimportant to the argument of this essay, since I will be concerned solely with the relation between the symbol level and the physical level, regardless of whether the symbol level is semantically interpreted or interpretable. [return to text]
7. When I gave a talk from which this paper is derived to a group of psychologists, one of them, Myra Smith, pointed out that the sort of situation I've described never really arises in practice, i.e. that it never really happens that competing theories are wholly equivalent with respect to their behavioral predictions. While this is most assuredly true, restricting attention to actual cases of empirically motivated choices among competing theories would obscure what I take to be the essential issue. For I think the essential issue, here, concerns the logical requirements for using empirical evidence to motivate such a choice. And I think that the problem regarding these logical requirements can only be brought out with thought experiments involving computational theories which do involve equivalent behavioral predictions. Thus, the problem with which I'll be concerned is one pertaining to the logic of confirmation. [return to text]
8. Pylyshyn mentions two other types of evidence for (dis)confirming computational theories (or what he calls 'empirical constraints' on computational theories). Neither of them, however, represent promising empirical methods. This is a point which I will take up more explicitly in the concluding comments. [return to text]
9. It might be thought that this follows only if token physicalism and type physicalism are the only physicalist options, and that supervenience represents a physicalist option I'm not considering. But I am apparently missing something in all the fuss over supervenience, since I don't think it's a physicalist doctrine at all. Consider Leibnizian Psycho-physical Parallelism. Given this sort of ontology, there would not be (indeed, could not be, given the principle of sufficient reason) any difference in the world without there being a physical difference in the world. Hence, according to Leibnizian Psycho-physical Parallelism, mental states supervene on physical states; but it's a dualist metaphysics nonetheless. So supervenience is compatible with dualism.
Haugeland (1983) has responded to this sort of consideration in an attempt to defend the idea that supervenience is indeed a physicalist doctrine. But he rejects parallelism by arguing that it is "theoretically unmotivated, magically undetectable and thoroughly bizarre" (1983, p. 9) and then invoking the methodological principle, "'Don't get weird beyond necessity'" (1983, p. 9). While I think these may be adequate grounds for a rational dismissal of parallelism, the problem for Haugeland is that these grounds have nothing to do with supervenience; they could be combined with any metaphysical commitment. Thus, Haugeland doesn't show that supervenience is incompatible with parallelism, he shows merely that parallelism is incompatible with the methodological principle he conjoins with supervenience. This, unfortunately, doesn't come anywhere close to showing that supervenience is a form of physicalism; and, indeed, I think the parallelism case shows that it's not.
If the foregoing is right, then I needn't be concerned with supervenience in what follows, since the physical symbol system hypothesis (and hence cognitive science) is committed to physicalism. If the foregoing is wrong, however, it really doesn't matter. For the argument I will develop will show that token physicalism is too weak a form of physicalism to underwrite the use of relative complexity evidence in the (dis)confirmation of computational theories. So, since supervenience is taken (by Haugeland, for example) to be a weaker form of physicalism than even token physicalism, it would follow that supervenience is likewise too weak a form of physicalism to underwrite the use of relative complexity evidence. [return to text]
10. This proposal is very similiar to Richard Miller's theory of confirmation (1987, chap. 4). [return to text]
11. In deductivist terms, this assumption means that a bit of empirical data is relevant evidence with respect to a choice among competing theories only if a (predictive) description of that bit of data can be deduced from at least one of the competing theories (together with auxiliary hypotheses, of course), but cannot be deduced from at least one of the other competing theories. In Bayesian terms, it means that a bit of empirical data is relevant evidence with respect to a choice among competing theories only if it's true of at least one of the competing theories that its conditional probability given that bit of data is greater than the probability of the theory alone, but false of at least one of the others. In bootstrapping terms, it means that a bit of empirical data is relevant evidence with respect to a choice among competing theories only if there is at least one of the competing theories for which an instance of a hypothesis in that theory can be deduced from a description of that bit of data together with other hypotheses in that theory, but there is at least one of the other theories for which this doesn't hold. [return to text]
12. I will be assuming throughout that state-talk and event-talk are interchangeable. Thus, if the reader prefers, event-talk can be substituted for state-talk in the following arguments, without affecting the conclusions. [return to text]
13. In other words, whether it is grossly implausible to think that type identities can be established between terms of the special sciences, such as 'monetary exchange', and predicates of physics is really beside the present purposes. Whether such wholly general considerations provide strong support for token physicalism as a general metaphysical doctrine is not my concern. I am concerned only with what these doctrines entail with respect to the relation between symbol-level descriptions and physical-level descriptions of a physical symbol system. So, I will be using 'token physicalism' and 'type physicalism' as terms for these implications; I will not be using them in their general sense. And I don't take the conclusions of this paper to imply anything whatsoever about the reducibility of economics, say. [return to text]
14. Friends of functionalism who favor token physicalism may think that I have missed the point here, since token physicalism can allow that the very same computational processes that constitute human cognition could be realized in physical systems which have precious little in common with the human organism. Hence, it might be thought that I am being 'chauvinistic' to say that token physicalism holds that every state over which a computational theory generalizes is a brain state. But my concern in this paper isn't with the philosophy of mind, it is with computational explanations of human cognition. And, since human cognition is what's at issue, the physical system in which human cognition is realized is most assuredly the human brain. No one -- not even a token physicalist -- should find this problematic. [return to text]
15. A few things need to be said, here, about what I'll be calling 'type physicalism'.
First, type physicalism is actually somewhat stronger than I've characterized it. I've characterized it as being committed only to correspondences between types of computational state and types of neurological state. But type physicalism is actually committed to the identities of types of computational state and types of neurological state, which of course entails a correspondence between the types of state in a computational taxonomy and types of state in a neurological taxonomy. Since only the correspondence between types will be important for the arguments to follow, I will focus on it.
Second, it would be useful to distinguish between what might be called 'strong type physicalism' and 'weak type physicalism'. Strong type physicalism could be characterized as the doctrine that every type of computational state corresponds to some type of physical state. Thus, according to strong type physicalism, if the martian cognitive system were computationally equivalent to ours, the types of computational state which describe both cognitive systems would correspond to the same type of physical state in both cases. This is the view which is usually the target of criticism when martians are introduced into the debate; for, the argument usually goes, martians could conceivably be physically quite distinct from us, even though we shared equivalent computational profiles. I want to distinguish strong type physicalism, however, from weak type physicalism, which could be characterized as the doctrine that every type of computational state in some (natural) kind of system corresponds to some type of physical state in that kind of system. Thus, according to weak type physicalism, the correspondences between types of computational state and types of physical state are relativized to natural kinds. (Even though it is often the target of criticism, I don't know of anyone who actually subscribes to strong type physicalism. What I'm calling 'weak type physicalism' is essentially the view held by Lewis (1980a, 1980b, 1980c) and Kim (1980).) Now, although the natural kinds to which these correspondences are relativized are taken to be species (Lewis 1980c), in what follows I don't want necessarily to make that assumption. I think that a potentially more useful way of viewing the situation allows the natural kinds to be anatomical rather than biological. The reason for this is that it provides, I think, a more useful way of accounting for things like tensor network theory (Churchland 1986, pp. 412-450), a computational theory which explains the functioning of the cerebellum; as such, tensor network theory is true of any species which possesses a cerebellum.
There is, however, a form of type physicalism even weaker than weak type physicalism -- roughly the view that Haugeland (1990, pp. 388-389) calls 'local congruence'. On this view, type identities are relativized to individuals rather than (anatomical or biological) natural kinds. I will argue, however, that computational theories can be (dis)confirmed only if there are type-type correlations between postulated computational states and the brain states which realize them. And this implies that, if computational theories are to be (dis)confirmed, the level of generality of the type-type correlations must be commensurate with the intended level of explanatory generality of the theories. So, if local congruence obtains, computational theories of individual cognitive subjects can be (dis)confirmed. I take it, though, that the goal of cognitive science is to explain human cognition -- that is, to uncover species-wide cognitive regularities -- and not simply to explain individual cognitive profiles. So, since I will be arguing that relative complexity evidence can (dis)confirm computational theories of human cognition only if weak type physicalism is true, it will follow that 'local congruence' is too weak a form of type physicalism to support this use of relative complexity evidence. Indeed, for these purposes, it is in effect no stronger than token physicalism. This will become clearer, however, as the argument proceeds. (I am indebted to John Haugeland for making me aware of these points.)
Finally, according to weak type physicalism, the types of state in a neurological taxonomy themselves constitute natural kinds. Thus, any theory which claimed a correlation between a computational state type and an indefinitely long disjunction of brain states would ipso facto be a form of token physicalism, since an indefinitely long disjunction of states doesn't constitute a natural kind. Such a correlation does nothing more than associate distinct tokens of the computational state type with tokens of distinct brain state types. [return to text]
16. In the passage quoted, Pylyshyn suggests the number of elementary, intermediate steps as a measure of difficulty only for the computational theories. I want first, however, to consider the most general possible use of this measure and show that it can't perform the general task of ranking problems for both theories and human subjects. Shortly I'll consider the possibility of using it only to rank problems for theories and how this ranking could (putatively) be compared with a ranking of problems for human subjects derived from a different measure of difficulty. [return to text]
17. Dreyfus (1979, pp. 102-103), for example, appeals to such protocols in claiming that chess-playing programs don't provide adequate explanations of human chess-playing ability. [return to text]
18. Shortly, the discussion will turn to processing times as measures of the complexity of cognitive tasks. But, it should be noted at this point that processing time measures would be unreliable indicators of the character of what Ericsson and Simon call 'non-automatic' processes. The reason is simply that the durations of any processes which are directly under conscious control vary greatly from subject to subject, and from time to time with the same subject, due to the possibility of distractions, fatigue, nervousness, etc. Thus, the use of processing time measures would be reliable indicators only of the character of 'automatic' processes (i.e. processes which are not under conscious control) or what Fodor (1983) has called 'modular' processes. Consequently, this type of evidence could only be relevant to the confirmation of computational models of such modular processes. This implies, by the way, that the only cognitive phenomena which are susceptible to (confirmable) computational explanation are the modular processes, and that there will be no computational explanations of central (conscious) cognitive processes (a conclusion which Fodor draws on independent grounds). [return to text]
19. Simon (1978, p. 501) and Pylyshyn (1984, p. 126) in fact equate the time taken to solve a problem with the number of elementary steps involved in its solution. But, as I will argue shortly, equating processing time measures of difficulty with measures of difficulty based on the number of elementary, intermediate steps is precisely what requires the truth of type physicalism. [return to text]
20. It is worth noting, at this point, that the results of this argument aren't simply an artifact of the GOFAI conception of cognition which involves serial search. A precisely parallel argument would work if it were assumed that the competing theories were PDP models together with a token physicalist interpretation of the states over which they generalize, since there would be numerous strongly inequivalent PDP models which explain the same cognitive capacity, and processing time evidence would be unable to discriminate among them given a token physicalist interpretation of their states. [return to text]
21. The invocation of Churchland's co-evolutionary research ideology may appear a bit strange in a context in which I have been arguing for type physicalism, since type physicalism would seem to support smooth reductions of one level of description to another and Churchland supports the elimination of one level of description in favor of the other. But this invocation of Churchland is strange only if one fails to keep distinct the levels of description which are being smoothly reduced or eliminated. When Churchland speaks of elimination, she has in mind the everyday intentional level of description, which may provide semantic interpretations of the symbol-level description of a physical symbol system. But Churchland also is committed to the idea that the brain is a computational system of some sort (see, e.g., her favorable review of tensor network theory [1986, pp. 412-450]). There is only a tension between these two stances if one persists in thinking that all computational theories of cognition are semantically interpreted or interpretable by the everyday intentionalistic vocabulary. If one gives up this idea, then there is a sense in which a computational theory of human cognition could simultaneously eliminate the intentionalistic vocabulary and support type identities between the states over which it generalizes (at the symbol level) and brain states. And this would be the character of any computational theory which was amenable to such type identities and which was such that its symbol level was not semantically interpretable by the intentionalistic vocabulary. Thus, to reemphasize what I've stated earlier, my concern with type physicalism in this essay is a concern only with respect to the relation between the symbol level of a computational theory and the physical-level description of the system of which that theory is true. [return to text]
22. It might be thought that this admits of an easy refutation based on the restoration of function phenomenon, which occurs when someone suffers damage to a part of the brain which subserved some cognitive function and later has that cognitive function restored, but now subserved presumably by some different part of the brain. This phenomenon can be interpreted as indicating that the very same cognitive processes which were previously realized by one brain process are subsequently realized by a different brain process; and this interpretation would seem to support token physicalism. But I don't think that this interpretation of the situation must be accepted. There are, I think, two other ways one could go. First, one could bite the bullet and claim that, contrary to apparent similarities, the previous and subsequent cognitive processes are in fact distinct. Second, one could claim that, contrary to apparent differences, the previous and subsequent brain processes which realized this cognitive process are in fact of the same type. Going this second route would involve giving up the idea that type-type correlations between computational states and brain states can only be established if the same computational state is always realized by the same neuron, say. So, it seems to me, the token physicalist interpretation of the restoration of function phenomenon is plausible only given a very crude conception of how brain states themselves are individuated. In this connection, current work on PDP models may provide hitherto-unthought-of ways of individuating brain states -- ways which would allow for type-type correlations even in the face of such things as the restoration of function phenomenon. [return to text]
23. I am indebted
to Arthur Fine and Meredith Williams for numerous conversations about the
ideas in this essay and for helpful comments on a previous draft. I am
also indebted to J. D. Trout for very helpful comments on a previous draft
(comments which were so numerous I couldn't possibly account for all of
them), to John Deigh and an anonymous referee for comments on a previous
draft, and to Raysid Sanitioso and Alexander Nakhimovsky for helpful conversations.
My greatest debt, however, is to Tammy Lynn Alspector for discussing the
ideas with me at every stage and reading and commenting on every draft.
[return to text]
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