Are Connectionist Models Theories of Cognition?
Department of Psychology
M3J 1P3 CANADA
Connectionist models of cognition are all the rage now. It is not clear, however, in what sense such models are to be considered theories of cognition. This may be problematic, for if connectionist models are not to be considered theories of cognition, in the traditional scientific sense of the word, then the question arises as to what exactly they are, and why we should pay attention to them. If, on the other hand, they are to be regarded as scientific theories it should be possible to explicate precisely in what sense this is true, and to show how they fulfill the functions we normally associate with theories. In this paper, I begin by examining the question of what it is to be a scientific theory. Second, I describe in precisely what sense traditional computational models of cognition can be said to perform this role. Third, I examine whether or not connectionist models can be said to do the same. My conclusion is that connectionist models could, under a certain interpretation of what it is they model, be considered to be theories, but that this interpretation is likely to be unacceptable to many connectionists.
A typical complex scientific theory contains both empirical and theoretical terms. The empirical terms refer to observable entities. The theoretical terms refer to unobservable entities that improve the predictive power of the theory as a whole. The exact ontological status of objects referred to by theoretical terms is a matter of some debate. Realists believe them to be actual objects that resist direct observation for one reason or another. Instrumentalists consider them to be mere "convenient fictions" that earn their scientific keep merely by the predictive accuracy they lend to the theory. I think it is fair to say that the vast majority of research psychologists are realists about the theoretical terms they use, though they are, in the main, unreflective realists who have never seriously considered alternative possibilities.
Let us begin with a relatively uncontroversial theory from outside psychology -- Mendelian genetics. In the Mendelian scheme, entities called "genes" were said to be responsible for the propagation of traits from one generation of organisms to the next. Mendel was unable to observe anything corresponding to "genes," but their invocation made it possible for him to predict correctly the proportions in which succeeding generations of organisms would express a variety of traits. As such, the gene is a classic example of a theoretical entity. For present purposes, it is important to note that each such theoretical gene, though unobservable, was hypothesized to correspond to an individual trait. That is, in addition to the predictive value each theoretical gene provided, each also justified its existence by being responsible for a particular phenomenon. There were no genes in the system that were not directly tied to the expression of a trait. Although some genes were said not to be expressed in the phenotype (viz., recessive genes in heterozygous individuals), all were said to be directly involved in the calculation of the expression of a specific trait. That is to say, their inclusion in the theory was justified in part by the specificity of the role they were said to play. It is worth noting that the actual existence of genes remained controversial until the discovery of their molecular basis -- viz., DNA -- and our understanding of them changed considerably with that discovery.
Now consider, as a psychological example of theoretical entities, the model of memory proposed by Atkinson and Shiffrin (1971). It is a classic "box-and-arrow" theory. Information is fed from the sensory register into a holding space called Short Term Store (STS). If continuously rehearsed, a limited number of items can be stored there indefinitely. If the number of items exceeds the capacity of the store, some are lost. If rehearsal continues for an unspecified duration, it is claimed that some or all of these items are transferred to another holding space called Long Term Store (LTS). The capacity of LTS is effectively unlimited, and items in LTS need not be continuously rehearsed, but are said to be kept in storage effectively permanently. STS and LTS are, like genes, theoretical entities. They cannot be directly observed, but their postulation enables the psychologist to predict correctly a number of memory phenomena. In each such phenomenon, the activity of each store is carefully specified. The precision of this specification seems to be at least part of the reason that scientists are willing to accept them. Indeed, many experiments aimed at confirming their existence are explicitly designed to block, or interfere with the hypothesized activity of one in order to demonstrate the features of the "pure" activity of the other. Whether or not this could be successfully accomplished was once a dominant question in memory theory. The issue of short term memory effects being "contaminated" by the uncontrollable and unwanted activity of LTS occupied many experiments of the 1960s and 1970s.
Over the last 30 years the Atkinson and Shiffrin model has been elaborated and refined. As a result, the number of memory systems hypothesized to exist has grown tremendously. Baddeley (1992), for instance, has developed STS into a series of "slave systems" responsible for information entering memory from the various sense modalities (e.g., the phonological loop, the visuospatial sketchpad), the activities of which are coordinated by a "central executive." Tulving (1985), on the other hand, has divided LTS into four hierarchically arranged systems responsible for episodic memory (for personal events), semantic memory (for general information), procedural memory (for skills) and implicit memory (for priming). In order to establish the existence of each of these many theoretical entities, thousands of experiments have been performed, aimed at revealing the independent of activity of one or another by attempts to block the activities of the others. With the entry of computer models into psychology, the theories have become even more complex, using dozens of theoretical entities. A recent version of Chomskyan linguistic theory, for instance, postulates more than two dozen rules that are said to control the building and interpretation of grammatical sentences (see e.g., Berwick, 1985).
In each of the models I have described so far, each theoretical entity represents something in particular, even if that something is itself theoretical. The existence and properties of the entities represented are supported by empirical evidence relating specifically to that entity. In a typical connectionist model, however, there are dozens, sometimes hundreds, of simple units, bound together by hundreds, sometimes thousands, of connections. Neither the units nor the connections correspond to anything known to exist in the cognitive domain the network is being used to model. Similarly, the rules that govern how the activity of one unit will affect the activity of other units to which it is connected are extremely simple, and not obviously related to the domain that the network is being used to model. Ditto for the rules that govern how the weights on the connections between units are to be changed. In particular, the units of the network are not thought to represent particular propositional attitudes (i.e., beliefs, desires, etc.) or the terms or concepts that might be thought to underlie them. This is all considered a distinct advantage among connectionists. Neither the units nor the connections correspond to anything in the way that variables and rules did in traditional computational models of cognition. Representations, to the degree that they are admitted at all, are said to be distributed across the activities of the units as a group. Any representation-level rules that the model is said to use are likewise distributed across the weights of all of the connections in the network. This gives connectionist networks their characteristic flexibility: they are able to learn in a wide variety of cognitive domains, to generalize their knowledge easily to new cases, to continue working reasonably well despite incomplete input or even moderate damage to their internal structure, etc. The only real question is whether they are, indeed, too flexible to be good theories. Or whether, by contrast, there are heretofore unrecognized features of good theories of which connectionist models can apprise us.
Each of the units, connections, and rules in a connectionist network is a theoretical entity. Each name referring to it in a description of the network is a theoretical term in the theory of cognition that it embodies.1 With the previously described theories, it was evident that each theoretical entity had a specific job to do. If it were removed, not only would the performance of the model as a whole suffer, but it would suffer in predictable ways, viz., the particular feature of the model's performance for which the theoretical entity in question was responsible -- i.e., that which it represented -- would no longer obtain. The units and connections in a connectionist net -- precisely in virtue of the distributed nature of their activity -- need not bear any such relation to the various activities of the model. Although this seems to increase the model's overall efficiency, it also seems to undermine the justification for each of the units and connections in the network. To put things even more plainly, if one were to ask, say, of Berwick's (1985) symbolic model of grammar, "What is the justification for postulating RULE ATTACH-NOUN?" the answer would be quite straightforward: "Because without it nouns would not be attached to noun phrases and the resulting outputs would be ungrammatical." The answer to the parallel question with respect to a connectionist network -- viz., "What is the justification for postulating (say) unit 123 in this network?" -- is not so straightforward. Precisely because connectionist networks are so flexible, the right answer is probably something like, "No reason in particular. The network would probably perform just as well without it."2
If this is true, we are led to an even more pressing question: exactly what is it that we can actually be said to know about a given cognitive process once we have modeled it with a connectionist network? In the case of, say, the Atkinson and Shiffrin model of memory, we can say that we have confirmation of the idea that there are at least two forms of memory store -- short and long term -- and this confirmation amounts to a justification of sorts for their postulation. Are we similarly to say that a particular connectionist model with, say, 326 units that correctly predicts activity in a given cognitive domain confirms the idea that there are exactly 326 units governing that activity? This seems ridiculous -- indeed almost meaningless. Aside from the obvious fact that we don't know what the "units" are units of, we might well have gotten just as good results with 325, or 327 units, or indeed with 300 or 350 units. Since none of the units correspond to any particular aspect of the performance of the network, there is no particular justification for any one of them. Some might argue that the theory instantiated by the network is not meant to be read at this level of precision -- that it is not the number of units, specifically, that is being put forward for test, but only a network with a certain general sort of architecture and certain sorts of activation and learning rules. This seems simply too weak a claim to be of much scientific value. As Popper told us, scientists should put forward "bold conjectures" for test. The degree to which the hypothesis is subject to refutation by the test is the degree to which it is scientifically important. Even without accepting Popper's strong stand on the unique status of refutation in scientific work, this much remains clear: To back away from the details of one's theory -- to shield them from the possibility of refutation -- is to make one's theory scientifically less significant. Surely this is not a move connectionist researchers want to make in the long run. It might be argued that the mapping of particular theoretical terms on to particular aspects of the phenomenon being modeled is unnecessary; it may just be an historical accident, primarily the result of our not being able to keep simultaneous control of thousands of theoretical terms until the advent of computers.
The real question, however, seems to be about what one can really be said to have learned about the phenomenon of interest if one's model of that phenomenon contains far more terms that are not tied down to the "empirical plane," so to speak, than it does entities that are. Consider the following analogy: suppose that an historian wants to understand the events that lead up to political revolutions, so he tries to simulate several revolutions and a variety of other less successful political uprisings with a connectionist network. The input units encode data on, say, the state of the economy in the years prior to the uprising, the morale of the population, the kinds of political ideas popular at the time, and a host of other important socio-political variables. The output units encode various possible outcomes: revolution, uprising forcing significant political change, uprising diffused by superficial political concessions, uprising put down by force, etc. Among the input and output units, let us say that the historian places exactly 72 units which, he says, encode "a distributed representation of the socio-political situation of the time." His simulation runs beautifully. Indeed, let us say that because he has learned the latest techniques of recurrent networks, he is actually able to simulate events in the order in which they took place over several years either side of each uprising.
What has he learned about revolution? That there must have been (even approximately) 72 units involved? Certainly not. If the "hidden" units corresponded to something in particular -- say, to political leaders, or parties, or derivative socio-political variables -- that is, if the network had been symbolic, then perhaps he would have a case. Instead, he must simply repeat the mantra that they constitute "a distributed representation of the situation," and that the network is likely a close approximation to the situation because it plausibly simulates so many different variants of it.
It must be concluded that he has not learned very much about revolution at all. The simple fact of having a working "simulation" seems to mean little. It is only if one can interpret the internal activity of the simulation that the simulation increases our knowledge; i.e., it is only then that the simulation is to be considered a scientific theory worthy of consideration.
One way we cognitive scientists might try to avoid the fate of our hypothetical connectionist historian is to claim that connectionist units do correspond to something closely related to the cognitive domain; viz., the neurons of the brain. Whether this is to be considered an analogy or an actual literal claim is often left vague by those who suggest it. Most connectionists seem wary of proclaiming too boldly that their networks model the actual activity of the brain. McClelland, Rumelhart, and Hinton (1986), for instance, say that connectionist models "seem much more closely tied to the physiology of the brain than other information-processing models" (p. 10), but then they retreat to saying that their "physiological plausibility and neural inspiration...are not the primary bases of their appeal to us" (p. 11). Smolensky (1988), after having examined a number of possible mappings, writes that "given the difficulty of precisely stating the neural counterpart of components of subsymbolic [i.e., connectionist] models, and given the very significant number of misses, even in the very general properties considered..., it seems advisable to keep the question open" (p. 9). Only with this caveat in place does he then go on to claim that "there seems no denying, however, that the subconceptual [i.e., connectionist] level is significantly closer [emphasis added] to the neural level than is the conceptual [i.e., symbolic] level" (p. 9). Precisely what metric he is using to measure the "closeness" of various theoretical approaches to the neural level of description is left unexplicated.
The general aversion to making very strong claims about the relation between connectionist models and brain is not without good reason. Crick and Asanuma (1986) describe five properties that the units of connectionist networks typically have that are rarely or never seen in neurons, and two further properties of neurons that are rarely found in the units of connectionist networks. Perhaps most important of these is the fact that the success of connectionist models seems to depend upon the fact that any given unit can send excitatory impulses to some units and inhibitory impulses to others. Few neurons in the mammalian brain do this. Although it is certainly possible that more dual-action neurons will be found in the human brain, the vast majority of cells do not seem to have this property, whereas the vast majority of units in connectionist networks typically do. Even as strong a promoter of connectionism as Paul Churchland (1990, p. 221) has recognized this as a major hurdle to be overcome if connectionist nets are to be taken seriously as models of brain activity. What is more, despite some obvious but possibly superficial similarities between the structure of connectionist units and the structure of neurons, there is currently little hard evidence that any specific aspect of cognition is instantiated in the brain by neurons arranged in any specified connectionist configuration.
It would accordingly appear that at present the only way of interpreting connectionist networks as serious candidates for theories of cognition, would be as literal models of the brain activity that underpins cognition. This means, if Crick and Asanuma are right in their critique, that connectionists should start restricting themselves to units, connections, and rules that use all and only principles that are known to be true of neurons. Other interpretations of connectionist networks may be possible in principle, but at this point none seem to have appeared on the intellectual horizon.3 Without such an interpretation, connectionist modelers are left more or less in the position of our hypothetical connectionist historian. Even a simulation that is successful in terms of transforming certain inputs into the "right" outputs does not tell us much about the cognitive process it is simulating unless there is a plausible interpretation of its inner workings. All the researcher can claim is that the success of the simulation confirms that some connectionist architecture may be involved, and perhaps something very general about the nature of that architecture (e.g., that it is self-organizing, recurrent, etc.). There is little or no confirmation of the specific features of the network because so much of it is optional.
Now, it might be argued that this situation is no different from that of early atomic theory in physics. Visible bits of matter and their interactions with other bits of matter were explained by the postulation of not just thousands, but millions upon millions of theoretical entities of mostly unknown character -- viz., atoms. This, the argument would continue, is not so different from the situation in connectionism. After all, as Lakatos (1970) taught us, new research programs need a grace period in the beginning to get themselves established. Although I don't have a demonstrative argument against this line of thought, I think it has relatively little merit. We know pretty well what atoms are, and where we would find them, were we able to achieve the required optical resolution. Put very bluntly, if you simply look closer and closer and closer at a material object, you'll eventually see the atoms. Atoms are, at least in that sense, perfectly ordinary material objects themselves. Although they constitute an extension of our normal ontological categories, they do not replace an old well-understood category with a new ill-understood one.4
By contrast, the units of connectionist networks (unless identified with neurons, or other bits of neural material) are quite different. They are not a reduction of mental concepts, and as such give us no obvious path to follow to get from the "high level" of behavior and cognition to the "low level" of units and connections. That it is not a reductive position is in fact often cited as a strength of connectionism but, if I am right, it is also the primary source of the ontological problems that have been discussed here.
To conclude, it is important to note that I am not arguing that connectionist networks must give way to symbolic networks because cognition is inherently symbolic (see, e.g., Fodor & Pylyshyn, 1988). That is an entirely independent question. What I am suggesting, however, is that the apparent success of connectionism in domains where symbolic models typically fail may be due as much to the huge number of additional "degrees of freedom" that connectionist networks are afforded by virtue of the blanket claim of distributed representation across large numbers of uninterpreted units, as it is to any inherent virtues that connectionism has over symbolism in explaining cognitive phenomena.
Atkinson, R. C. & Shiffrin, R. M. (1971). The control of short-term memory. Scientific American, 225, 82-90.
Baddeley (1992). Working memory. Science, 255, 556-559.
Berwick, R. C. (1985). The acquisition of syntactic knowledge. Cambridge, MA: MIT Press.
Churchland, P. M. (1990). Cognitive activity in artificial neural networks. In D. N. Osherson & E. E. Smith (Eds.), Thinking: An invitation to cognitive science (Vol. 3, pp. 199-227). Cambridge, MA: MIT Press.
Crick, F.H.C. & Asanuma, C. (1986). Certain aspects of the anatomy and physiology of the cerebral cortex. In J. L. McClelland & D. E. Rumelhart (Eds.), Parallel distributed processing: Explorations in the microstructure of cognition (Vol. 2, pp. 333-371), MIT Press.
Fodor, J. A. & Pylyshyn, Z. W. (1988). Connectionism and cognitive architecture: A critical analysis. Cognition, 28, 3-71.
Lakatos, I. (1970). Falsification and the methodology of scientific research programmes. In I. Lakatos & A. Musgrave (Eds.), Criticism and the growth of knowledge, (pp. 91-196). Cambridge, UK: Cambridge University Press.
McClelland, J. L., Rumelhart, D. E., & Hinton, G. E. (1986). The appeal of parallel distributed processing. In D. E. Rumelhart & J. L. McClelland (Eds.), Parallel distributed processing: Explorations in the microstructure of cognition (Vol. 1, pp. 3-44). Cambridge, MA: MIT Press.
Smolensky, P. (1988). On the proper treatment of connectionism. Behavioral and Brain Sciences, 11,1-73.
Tulving, E. (1985). How many memory systems are there? American Psychologist, 40, 385-398.
This paper was written while the author was the beneficiary of a grant from the Natural Sciences and Engineering Research Council of Canada. A considerably longer version of it has appeared previously in the electronic journal Psycoloquy (ftp://ftp.princeton.edu/pub/harnad/Psycoloquy/1998.volume.9/), where it can be found in the company of over a dozen commentaries and replies. The author would like to thank André Kukla, John Vervaeke, Michael Gemar, and Philip Groff (all affiliated with the University of Toronto), as well as Steven Harnad (of the University of Southampton) and his Psycoloquy review team for their helpful comments on earlier drafts. Requests and comments can be directed to the author at the Department of Psychology, York University, Toronto, Ontario, Canada, M3J 1P3, or to his e-mail address: email@example.com.
1. A Psycoloquy reviewer of this paper suggested that it is not the individual units that are theoretical entities, but only the units as a general type. He explicitly compared the situation to that of statistical dynamics, in which the phenomena are said to result from the actions of large, but unspecified, numbers of molecules of a general type. The difference is, of course, that we have lots of independent evidence of the existence of molecules. We know quite a lot about their properties. The same cannot be said of units in connectionist networks. Their existence is posited solely for the purpose of making the networks behave the way we want them to. There is no independent evidence of their properties or their existence at all.
2. Notice that a version of the Sorites paradox threatens here. There must come a point where the subtraction of a unit from the network would lead to a decrement in its performance, but typically connectionist researchers work well above this level in order to optimize learning speed and generalization.
3. One Psycoloquy referee suggested that units might correspond to small neural circuits rather than individual neurons. This might be so, but the evidential burden is clearly on the person who makes this proposal to find some convincing empirical evidence for it.
4. There may be a temptation to attempt to carry this through to the quantum level, and claim that it does not carry through at that level because of the physical impossibility of seeing subatomic particles. First of all, relying on our intuitions about the quantum world to illuminate other scientific spheres is a very dangerous move because it is there more than anywhere that our intuitions seem to fail. Despite this, the move would fail in any case because the impossibility at issue is merely physical, not logical. In a world in which light turned out to be continuous rather than particulate, the argument would carry through perfectly well. Put less technically, we know where to see subatomic particles, we just don't know how to see them. The same cannot be said for units in connectionist networks. They simply don't seem to refer to anything in the system being studied at all.