But Is It Science?
|The awakenings of the 1960s led most psychologists to a search for relevance and to commerce with such concepts as cognition, volition, and consciousness. For many of them, positivism and operationism became dirty words because of the gossip that, back home in philosophy, they were in trouble. This development did psychology great harm.|
--Gregory Kimble (1994, p. 257)
There can be no historical doubt that behaviorism has advanced ethology as a science, whereas the methods advocated by cognitivists have yet to prove their worth. Until mental concepts are clarified and their need justified by convincing data, cognitive ethology is no advance over the anecdotalism and anthropomorphism which characterized interest in animal behavior a century ago, and thus should be eschewed.
Cooperation merely depends upon the behavior of one animal serving as a stimulus that elicits a certain response from the other.
Must cognitive ethologists rely forever on anecdotal cognitivism and face the ensuing charge of anthropomorphism? Is it possible to investigate mental phenomena in nonhuman animals under natural conditions? Some critics believe that any attempt to investigate the minds of animals must fail to be scientific. Others object specifically to the methods of cognitive ethologists, especially the limitations inherent in fieldwork. Griffin´s books have failed to reassure critics that the problems facing cognitive ethology can be solved. Although he provides many examples of behaviors that are suggestive of mental processing, Griffin does not present an adequate theoretical framework for the attribution of mental states.
Here we consider a number of objections to the aims of studying animal cognition and mind that have been raised from within psychology. It is our view that some of these objections are based on differences in vocabulary, but where there are substantive disagreements we hope to make them clear. Later in this chapter we shall outline a framework for the attribution of mental states.
Kimble (1994, quoted above) reports as gossip the idea that in the 1960s positivism and operationism were in trouble back home in philosophy. But it was not mere gossip. Quine (1953) had already argued that the logical positivists´ theory of meaning relied on principles that were not justifiable from within the positivist framework, and that empirical science and theoretical philosophy are strongly intertwined. Quine revived the following thesis, which he attributed to Pierre Duhem: No scientific hypothesis is ever tested independent of an ensemble of mathematical, logical, theoretical, and empirical beliefs; consequently, the results of any experiment can never be taken as logically refuting any specific hypothesis, only as logically refuting the ensemble as a whole.
These troubles for positivism resulted in a broader conception of the relation between theory and evidence than is allowed by strict operationism. According to strict operationism, any theoretical term must be directly defined in terms of observable phenomena. But if no hypothesis is ever tested in isolation, the failure of an experimental prediction can always be attributed to any of the numerous assumptions that were used to generate the prediction. Any particular theory may be implicated in a large number of predictions, and the rejectability of the theory does not depend on its involvement in the failure of any single prediction. In view of the logical structure of this situation, as elaborated by the Quine-Duhem thesis, there is no objective reason for denying scientific status to theoretical terms that are not directly operationalized.
This view of the relationship between theory and evidence suggests that there are not likely to be any behavioral litmus tests for the attribution of mental states to animals, and that such attributions can be evaluated only in the context of a broad set of observations. Such a view is fully compatible with a thoroughly naturalistic account of mental phenomena that completely rejects dualist ideas about immaterial souls and other supernatural substances. Nonetheless, the idea that there is any room for such notions in science continues to provoke a vigorous negative response from a broad range of psychologists.
It is easy for philosophers of mind to label these responses "behaviorist" and to dismiss them all as results of a conditioned association of mentalistic terms with dualism. Unfortunately, the label "behaviorist" obscures some important distinctions among psychologists. In many cases, however, it does seem that scientists who resist the use of mentalistic terms are reacting against a perceived return to mysterious immaterial causes rather than responding to the careful suggestions that naturalistically inclined philosophers are making. This represents an unfortunate miscommunication about what is really at stake in this dispute.
Such miscommunication is apparent in Howard Rachlin´s (1991) discussion of cognitive ethology in his textbook of behavioristic psychology. Rachlin specifically discusses Dennett´s (1983) methodological suggestions for cognitive ethologists. Dennett suggests that ethologists frame hypotheses within a hierarchy of intentional attributions. Zero-order explanations of behavior involve only stimulus-response mechanisms. First-order explanations invoke representations of non-intentional facts about the world to explain behavior; for instance, a monkey´s ascent into a tree might be explained by the first-order belief that a leopard is present. Second-order explanations involves representations of first-order intentional facts, such as the belief that a leopard wants to eat me. Third-order intentionality involves representation of second-order facts. And so on. Rachlin reports this proposal as a suggestion about levels of consciousness, thus obscuring the distinction between intentionality and consciousness that is so important to much contemporary philosophy of mind (including Dennett´s). Rachlin proceeds to reject Dennett´s proposal on the ground that the ordinary notion of consciousness is of no scientific value. But Dennett (1991) would agree that the ordinary Cartesian notion of consciousness is of no scientific value, so this critique misses its target by a wide margin.
Cognitive ethologists need not be particularly embarrassed if they are unsure how to pursue questions about animal consciousness. The strategy of condemning cognitive ethology because it has trouble with consciousness is about as creditable as the strategy of so-called creation scientists who seek to undermine astronomy by pointing out that astronomers can´t explain what caused the Big Bang. There is much more to astronomy than that, and there is much more to cognitive ethology than questions about animal consciousness.
It is all too easy for participants on both sides of this debate to lapse into name calling, and drawing analogies with religious arguments seems to be a favored strategy. Indeed, the charge of anthropomorphism (Humphrey 1977; Colgan 1989; Kennedy 1992) often leveled against those who would attribute mental states to animals hearkens back to theological disputes about attributing human characteristics to divine beings (Mitchell 1996). Blumberg and Wasserman (1995) also play the religion card against Griffin. They claim that his argument from the complexity of animal behavior for animal mind is analogous to the argument from design for the existence of a creator. But the analogy fails: creators are outside nature (almost by definition), but neither Griffin nor other cognitive ethologists are opposed to naturalistic accounts of mental phenomena. Thus, there is less prima facie reason to be suspicious of inferences from apparently intelligent behavior to the intelligence of the actors.
We shall do our best to avoid these religious wars and instead examine the arguments offered by critics of attempts to study animal mind to see whether they really do support the conclusions that are claimed.
Many scientists who are sympathetic to the idea that nonhuman animals possess mental states are nonetheless skeptical of cognitive ethology. Underlying this view is the worry that we can never know about the mental states of others. In its most general form, this worry is the same as that traditionally known to philosophers as the problem of other minds. Psychologists concerned with human behavior effectively shelve skepticism about other minds in just the same way that physicists shelve skepticism about the mind-independent existence of physical objects. But many behavioral scientists believe that knowledge of nonhuman minds poses special problems. While they admit that knowledge of other human minds is possible, they regard the mental states of other animals as closed to us forever. To distinguish this from the general problem of other minds, we will refer to this as the other-species-of-mind problem.
The other-species-of-mind problem underlies the frequent complaint that attributing mental states to nonhumans is unjustifiable anthropomorphism--defined as an interpretation of what is not human in terms of human characteristics (see Fisher 1996 for a sophisticated analysis of this complaint). The charge of anthropomorphism clearly invokes the other-species-of-mind problem rather than the generic problem of other minds, since attributing mental states to other humans cannot, by definition, be considered anthropomorphic.
A very general argument against scientific knowledge of other minds can be reconstructed as follows (see Williams 1992 and Kimble 1994 for examples that follow this pattern):
|Mental phenomena are private phenomena.|
Private phenomena cannot be studied scientifically.
Thus, mental phenomena cannot be studied scientifically.
The first thing to note about this argument is that its premises depend on a particular conception of mental phenomena, namely that they are "private," and one might ask what this amounts to. Clearly, none of us is capable of directly seeing, touching, hearing, tasting, or smelling the mental states of others. But neither can any of us directly sense quarks. Thus, if all that "private" means is "not directly sensible," quarks are private phenomena too. Scientific understanding of quarks is based on what philosophers call inference to the best explanation: the selection of the most plausible hypothesis among competing alternatives for the explanation of observable phenomena. In the absence of further reasons against taking a similar approach to mental phenomena, the argument from privacy is not convincing. If "private" means "directly sensible only by the individual having the experiences," then inference to the best explanation would still seem to be a viable strategy. Indeed, it would fail to be a viable strategy only if the privacy of a mental state meant that it had no effects whatsoever beyond the individual subject possessing the state. Even if there is no conceptual reason why mental states must have effects (as Strawson (1994) has argued), it does not follow that there are no effects. And if they do have effects, it should be possible to discover the characteristics of mental states by an inference to the best explanation of those effects.
The first premise of the argument is probably untrue if "private" means "having no effects whatsoever," yet the second premise is true only if "private" is given that meaning. Thus, either the first premise is false or the second one is, and either way the argument is unsound. Because this version of the argument says nothing specifically about nonhuman animals, it would also rule out attempts to study human mental states--a view that is strongly at odds with contemporary cognitive science. A more restricted version of the argument must be considered for application to nonhuman subjects, viz.:
|Mental phenomena are private phenomena.|
Private phenomena cannot be studied scientifically in nonhuman animals.
Thus, mental phenomena cannot be studied scientifically in nonhuman animals.
In this version, the second premise makes special appeal to the fact that our subjects are nonhuman animals. Perhaps, a proponent of it might argue, one can infer the presence of mental states in humans, but one cannot do so for nonhuman animals. A commonly stated basis for this view is that, in the absence of language use by nonhumans, their behavior is not discriminating enough to allow the attribution of mental states. (For examples of this claim see p. 115 of Frey 1980 and p. 40 of Rosenberg 1990.)
We do not intend to get embroiled in the dispute about what constitutes a language and whether nonhuman animals meet the criteria for language possession. In fact we shall have very little to say about attempts to teach artificial languages to nonhuman animals (although in later chapters we shall discuss natural systems of animal communication and the role of human language in specifying mental content). Our aim here is simply to point out that in view of our diagnosis of the state of the discussion, it is up to cognitive ethologists to explain the grounds on which a mentalistic explanation might be considered the best explanation of some aspect of animal behavior. Griffin, relying on little more than the methods of anecdotal cognitivism, has not been entirely successful in doing this (Bekoff and Allen 1996). Progress will be made by identifying various aspects of mentality and showing how each of these aspects might be made amenable to scientific investigation. This, however, is the project of later chapters. Here we shall continue to examine the arguments of critics.
The Behaviorist Challenge
Often philosophers to whom we talk about cognitive ethology are surprised to learn that behaviorism is alive and well in studies of animal behavior. Yet it is. For example, Blumberg and Wasserman (1995, p. 142) chide Allen and Hauser (1991) for having "prematurely announced the demise of behaviorism." McFarland and Bösser (1993, p. 289) write that "the problem for the ethologist is that for every cognitive account of an animal´s behavior there is always an equally valid behaviorist account." Coupled with the presumption that considerations of simplicity and parsimony favor behavioristic accounts, prospects for mentalistic explanations can be made to appear quite bleak. There are many of our readers, including philosophers and scientists, who will not have much sympathy with behaviorism. But despite the impression of many that behaviorism collapsed under its own weight, many of its methodological presuppositions continue to exert an influence on the thinking of many scientists about issues of animal mind. We will take some time to clarify these issues.
There is a tendency by philosophers of mind and others outside of psychology to lump all the variants of behaviorism together. Within psychology, however, the differences among followers of Pavlov, Watson, Skinner, Hull, and Tolman are very important. Arguments endorsed by one group would not necessarily be endorsed by the members of another group (Smith 1986; Kamil 1987). We will attempt to tread carefully by discussing the arguments of individual authors on their own merits.
In the passage quoted at the beginning of this chapter, Kimble (1994) self-consciously portrays the second coming of J. B. Watson. We have already mentioned that the demise of positivism in the philosophy of science cannot seriously be dismissed as "gossip." Yet Kimble´s main argument for why psychology must be behavioristic (1994, p. 258) is based on just this dismissal:
|If psychology takes the scientific road to truth, it will discover that the only observables available are stimuli and responses. That reality means that, at bottom, psychology must be behavioristic. After that, it can be as biological, cognitive, or even humanistic as it wants to be. But disciplines that study something else--like brain, mind, or human potential--without connections to stimuli and responses may occasionally be science--even elegant science--but they are not psychology. Psychology is the science of behavior.|
The transition from what is observable to what may be theorized is not justified. Although cognitive or biological approaches to mind may employ theoretical notions that are not operationally connected to observable stimuli and responses, this is not the same as saying that they have no connection to observables. To suggest otherwise is to attack a straw man, for few present-day theorists deny that there are connections. At issue is the nature of the connections between theoretical terms and observable phenomena. Positivist theories of the nature of science and meaning were beautiful theories; they were, however, ultimately indefensible (Quine 1953), and no amount of lamenting that fact can change it. Once it is realized that few theoretical notions can be strictly operationalized, the inference from what is observable to what is acceptable as a theoretical posit must be seen in terms more sophisticated than Kimble´s. What applies to psychology in this regard applies also to cognitive ethology.
We have already stated our view that mental-state attributions, when justified, are justified by inference to the best explanation. To understand any such inference, it is necessary to understand what is being explained and what the alternative explanations are. In human psychology, it is sometimes possible to take the existence of mentality for granted and to make the mental states themselves targets for explanation (Shapiro 1994). However, ethologists are not in a position to take mental states of animals for granted. Furthermore, because ethology is traditionally the comparative study of behavioral phenotypes, it is not surprising that cognitive ethologists regard behavior as their main target for explanation.
Animals face a variety of environmental conditions that change over a range of time scales. Conceivably it could be advantageous for a given piece of behavior to be "stimulus bound" in the sense that it occurs invariably (or almost invariably) in response to some stimulus. However, in many cases stimulus-bound behavior will not be to an organism´s best advantage. For example, it does a sated animal no good to continue to eat when its visual and olfactory systems are being stimulated in a way that normally corresponds to the presence of food. Thus, organisms have internal states that modulate their responses to such stimuli. Indeed, laboratory researchers must often take account of this in the design of their experiments. Many laboratory protocols involve lowering the body weight of animals in order to produce the proper state of "motivation" to work for a food reward.
In admitting the notion of "motivation," one agrees that explanations of behaviors must take into account factors that are internal to the organisms in question. Grounds for disagreement lie in the questions of how complex these internal factors may be and how they are best described. In chapter 2 we touched on the controversy between Hull and Tolman about the status of intervening variables in the explanation of animal behavior. Those who are sympathetic to the Hullian line tend to regard internal factors either as further "internal stimuli" or as simple threshold mechanisms that are relatively isolated from one another. However, in some organisms at least, these internal factors seem to be very complicated indeed. For example, an organism´s response to a given stimulus may change as a result of a single experience with an entirely different stimulus at a different time and location. Humans provide clear examples; for instance, a news report about a natural disaster close to home may make an individual more likely to pick up the next telephone he or she encounters. Comparative studies of the extent to which the behavior of nonhuman organisms toward a given stimulus may be affected by stimuli of a rather different type are needed; however, tests of observational learning are of particular interest in this respect, for in such cases an organism may acquire a new behavior on the basis of no direct reward.
The degree of interaction between external and internal factors can be conceptualized as falling along a scale. Toward one end of the scale, external stimuli predominate over internal factors and the behaviors can be considered relatively "stimulus bound"; toward the other end, internal factors predominate over external stimuli and the behaviors may be considered relatively "stimulus free." Behavioristic explanations are to be preferred at or near the end of the scale where external factors predominate over internal factors in the causation of behavioral responses. "Predominate" has two senses here, referring both to the extent to which external stimuli that reliably produce a given response can be identified and to the extent to which explanations of behavior tend to focus on the adequacy of those external factors in accounting for the observed behavior.
Toward the stimulus-free end of the scale, it is necessary to invoke internal factors to account for the observed behaviors. These internal factors may be of varying degrees of structural complexity, understood both in terms of the number of different types of internal events and in terms of the types of possible interactions between tokens of these internal event types. Some relatively stimulus-free behaviors, such as quasi-diurnal cycles, may be explained by relatively simple and relatively isolated internal mechanisms, such as a physiological "clock." Cognitive and mentalistic explanations, by adopting typologies of internal states drawn (respectively) from computational theory and folk psychology, provide models for understanding types of complex interactions between internal states. As the example of an internal clock shows, we do not argue that every stimulus-free behavior should be explained cognitively or mentalistically. Rather, we argue, cognitive or mentalistic explanations may be preferred for stimulus-free behaviors that involve integrating inputs from various contexts over extended time scales.
Fodor (1994, p. 90) uses the term "stimulus free" in a way that is related to our use of it. Fodor is concerned, as we are, with the question which behaviors are best explained by attributing mental representations (with meaningful content) to organisms. According to Fodor, intentional states are causally intermediate between stimuli (p. 89: "the currently impinging environmental forces") and behavior, and can therefore be used to account for behavior that is relatively "autonomous" from environmental conditions. It is important to note here that stimulus conditions and environmental conditions should be strictly distinguished. The presence of a coral snake or a king snake will, under certain conditions, produce the same stimuli in an organism, yet these should be considered different environmental conditions because one snake is deadly and the other is not. This serves to make the point that organisms face the problem of using proximal stimuli to guide their reactions to more distal causes of those stimuli.
Fodor simply asserts that some human and some nonhuman behaviors are stimulus free. However, there is a long tradition in behavioristic circles of denying or downplaying the occurrence of behaviors that are not stimulus bound. Stimulus-bound phenomena prove to be especially suitable for laboratory investigation because of the ease with which the relevant stimulus conditions, and hence the behavioral responses, can be replicated. Indeed, the demands of statistical significance and repeatability tend to favor the study of stimulus-bound behaviors in laboratory settings over the observation of animals in natural habitats. Furthermore, behavioristic learning theory is essentially a theory of how behaviors are bound to stimuli, either by being paired with another stimulus (the unconditioned stimulus) to which the behavior was previously bound, as in classical conditioning, or by subsequent reinforcement of a contingent pairing of stimulus and behavior, as in instrumental or operant conditioning.
Although the terminology of stimulus-bound and stimulus-free behaviors is not found in ethology, the concept of stimulus boundedness is implicit in ethological research. The classical ethological concepts of releasers and sign-stimuli (Tinbergen 1951; Hailman 1967; Hinde 1970; Eibl-Eibesfeldt 1975) were used to explain and describe the tight link between the occurrence of a particular stimulus and the performance of a specific response. Numerous examples of behavior studied by classical ethologists count as relatively stimulus bound. The stereotyped responses of sticklebacks to moving red objects, hatchling gulls to beak models, and ants to objects daubed in oleic acid all provide good examples of relatively stimulus-bound behaviors that have been extensively studied by ethologists. These phenomena are especially suitable for laboratory investigation because of the ease with which the relevant stimulus conditions, and hence the behavioral responses, can be replicated. Classical ethology made the turn toward recognizing internal factors with the Lorenzian notions of "action-specific energy" and "drive," which, like Hullian intervening variables, seem to be modelable as simple accumulator-threshold devices. Although such notions are capable of explaining relatively simple internally motivated behaviors, the interactions they permit are far less complex than those suggested by the application of cognitive or mentalistic notions to the description of the internal states of animals.
For cognitive ethologists, however, behaviors that appear relatively stimulus free are often of great interest. For example, vervet monkeys whose behavior indicates that they have detected a predator do not automatically emit an alarm call. The existence of this "audience effect" has been used to argue in favor of a cognitive "referential" account of vervet communication (Seyfarth et al. 1980; Dennett 1983; Cheney and Seyfarth 1990). Likewise, the fact that rhesus macaques appear to scan for group members before deciding whether to give a food signal shows that they are not bound to call when they detect food (Hauser and Marler 1993a,b) and suggests (but requires further empirical investigation to establish) that these animals are aware of the informational content of their signals (Allen and Hauser 1993). Another example is provided by research showing that bees appear to take stored information about physical features of their environment into account in their responses to the dances of hive members (Gould 1986); this degree of freedom in bees´ responses has been cited as evidence for cognitive maps in bees (see Gould and Gould 1994). The interest in behavioral "novelty"--for example, macaques´ washing potatoes (Galef 1996a) and vervets´ soaking acacia pods in order to extract edible parts (Hauser 1988)--can also be understood as interest in stimulus-free behavior.
Some researchers have tended to downplay the importance of behavior that appears to be stimulus free, often by one of the following strategies:
|denying that the behavior in question is really stimulus-free Heyes, for example, has argued that many behaviors described in the literatures of cognitive ethology and comparative psychology can be explained by the presence of stimuli that were not controlled for in the experiments. In response to a study by Povinelli et al. (1990; see also Povinelli 1994a, 1996) showing that chimpanzees could look at photographs depicting humans trying to solve problems and select items that would enable the problems to be solved, Heyes (1994c; see also Heyes 1994d) suggests that the chimps´ performance might be explained by matching to sample. In other words, the photographs contained a sample of the right response, which is the stimulus that elicits the response. Another example of the same strategy applies to the observation that a lone vervet monkey confronted with a predator is much less likely to give an alarm call than one in a group (Cheney and Seyfarth 1990). The common response is to suggest that alarm-call production is actually under the control of a complex stimulus involving the conjunction of predator and conspecifics. We do not deny that in specific cases one may be able to provide a sound empirical case to support the claim that a behavior may be bound to a specific stimulus. However, many critics of cognitive accounts mount their criticism without making the relevant empirical case, relying on the fact that for any behavior it is always possible to imagine some (possibly complex) stimulus to which the behavior is bound that has escaped the notice of the researchers whose cognitive inferences are being questioned. Heyes (1994a) seems committed to the view that there must be such a stimulus even if we do not know what it is. This view can also be found in the writings of several earlier comparative psychologists (see Hearst 1975 for a discussion citing Konorski and Miller 1937a,b and Guthrie 1952). In the absence of the relevant empirical data, this could be viewed as a questionable methodological bias.|
attributing the behavior to chance With respect to the much-discussed case of potato washing in Japanese macaques (Galef 1996a), Heyes (1993) suggests that the alleged discovery that washed potatoes are better to eat may in fact have arisen when a potato was accidentally dropped by an individual who had entered the water for other reasons. Heyes then explains the fact that this individual adopted the practice of washing potatoes in terms of operant conditioning. Furthermore, she argues that it is a plausible explanation for the subsequent spread of the practice to other troop members that each of them went through a similar serendipitous process, perhaps accelerated by the tendency of monkeys to congregate (in this case, in the water). She uses this line of argument to deny the suggestion that observational learning was important in spreading the potato-washing technique. Observational learning presents a puzzle to some learning theories because it involves modification of a subject´s behavior by processes that do not involve direct reinforcement of that behavior. The appeal to chance is an attempt to avoid those puzzles. Indeed Heyes (1994b, p. 229) argues that it is possible to subsume various categories of social learning under standard paradigms for asocial learning, and that "perhaps . . . it is time also to reexamine the 'special´ status of social learning."
ignoring the variations in behavior as a consequence of statistical averaging This third way in which stimulus-free behaviors tend to get downplayed is a consequence of the common methodological practice of pooling data, a practice that serves to meet the demand that results be statistically analyzable. Many studies establish a statistically reliable connection between a given stimulus condition and a response, in the sense that (for example) subjects produce the response in 90 percent of stimulus presentations. The 10 percent of cases where the stimulus fails to produce the response tend to be ignored in the analysis. (Labeling observations as "anecdotes" and then dismissing them is also symptomatic of this concern with statistical reliability.) Yet, for really understanding the causal complexity underlying the production of behavior, we argue (chapter 7) that it is a mistake to dismiss these data as noise. Here interest in causal and evolutionary explanations converge. For selection to operate, there must be variance in the expression of a given phenotype. Therefore, it is crucial for ethologists not to dismiss such differences just because they are hard to treat statistically. Even if the number of individuals that make up the "noise" is small, there are ways to handle them rigorously.
Psychology, according to a standard dictionary definition, is the study of mind and behavior. For a major part of the twentieth century, psychology, especially comparative psychology, was on a behavioristic track that explicitly denied the possibility of a science of animal mind. This halving of psychology depended on unsound arguments about the privacy of mental phenomena and on views about the relationship between observation and theory that should be rejected. Although many contemporary studies of animal learning and memory adopt a cognitive approach, the influence of behaviorism is still evident in the writings of a number of behavioral scientists. The appearance of the adequacy of behavioristic explanations to account for any observed behavior (McFarland and Bösser 1993) may be an artifact of the way in which the behaviors to be explained are identified. When the full complexity of the behaviors is considered, behavioristic explanations can seem rather less straightforward than the cognitive or mentalistic alternatives. Byrne (1995, p. 134) makes this point forcefully:
|. . . for the 18 cases [of deception] that seem intentional, any one of them can still be challenged and an explanation devised that is based on a hypothetical series of coincidences in the past that might have given rise to learning by association. However, as the hypothesized coincidences become more and more far-fetched, and the histories of possible events that just might have reinforced these tactics grew longer and longer, we decided at some point it was simpler to accept that some primates can understand intentions.|