Everyone who has taken an undergraduate methodology course in psychology 'knows' what an operational definition is. It is practically an article of faith among psychologists that in order to conduct empirical research each of the variables under study must first be operationally defined. The story usually goes something like this: You want to study some psychological variable - say anger. You have no way of measuring anger directly so you measure some purported behavioral or physiological symptoms of the variable - say loudness of voice or blood pressure - as an indirect measure of anger. These indirect measures are taken to be the operational definitions of anger. Ideally, one collects several different measures in an attempt to 'triangulate' the psychological variable itself. Those with a particularly behaviorist (or, in this example, Jamesian) bent might assert that anger just is those behavioral or physiological expressions, but I think it is safe to say that most psychologists believe in the psychological reality of the state as well, even if they are unable to clearly state its precise ontology. [p. 292]
Unfortunately, this story has fairly little to do with operational definitions as they were proposed in the 1920s, and, further, there is fairly little in the way of rigorous argument to recommend it. Nevertheless, it has been propagated from one generation of psychologists to the next for the greater part of this century and continues to be taught in university psychology departments to the present day. Thus, it has become painfully evident to philosophers for some time that psychologists, by and large, are not well equipped when it comes to defending the epistemological and ontological assumptions which underlie their research and, if they turn out to be indefensible, that a great deal of psychological research might well rest on philosophical quicksand.
This lowly estimation of psychological research has been by no means confined to the sporadic outbursts of epistemological extremists. In the 1940s Wittgenstein (1953/1958) remarked that 'in psychology there are experimental methods and conceptual confusion' (p. 232). More recently Jerry Fodor (1968) noted that 'many philosophers secretly harbor the view that there is something deeply (i.e. conceptually) wrong with psychology' (p. vii). Not so secretly as Fodor might have it, Lakatos (1970) called the typical methodological practices of psychologists 'intellectual pollution' and 'machinery for producing phoney corroborations. . . where, in fact there is nothing but an increase in pseudo-intellectual garbage' (p. 176n.). Assuming a somewhat more moderate stance, Suppe (1984) has suggested that psychologists typically indulge in a 'serious misunderstanding of what the relationship ought to be between science and philosophy of science' (p. 90). The problem of operationism, I believe, exemplifies this misunderstanding.
As a start toward correcting this state of affairs, this paper
surveys and analyzes the history of the relationship between operationism
and psychology. The paper is divided into three sections. The
first outlines and discusses the origins and early development
of operationism. The second section explores its adoption and
adaptation by behavioristic psychologists in the 1930s and 1940s.
The third traces the decline of behaviorism since the time of
World War II. It is argued that behaviorism was, from early in
its development, based upon misunderstandings about operationism
and that its fall was due as much to these mistaken beliefs as
it was to the flaws of operationism itself. Although psychology
seems to have shed behaviorism of late, many of the old misunderstandings
have remained largely intact. I hope to increase the reader's
awareness of the importance of the role which philosophy of science
has played in the development of psychology during this century.
I hope, also, to provoke greater interest in these issues so that
more psychologists will pursue sophisticated analyses of the adequacy
and appropriateness of the various philosophical assumptions in
which psychological research is typically grounded.[p. 293]
1. The Origins of Operational Analysis
1.1 The Fall of Newtonian Physics
By the final years of the 19th century, empiricism had reached the high point of its influence in both science and philosophy. Under its aegis, physics had been so apparently successful that in 1900 Lord Kelvin made the astounding announcement to the Royal Institute in England that physics, as an academic discipline, had almost completed its work. The only significant puzzles that remained to be solved, according to Kelvin, were the black-body radiation problem and the Michelson-Morley experiment of 1887. Unbeknownst to Kelvin, the solutions to these two phenomena were to have a profound impact not only on physics but also on the most fundamental beliefs underlying all of science and epistemology.
Although not recognized until decades later, the Michelson-Morley experiment demonstrated the relativity of the speed of light, a finding undermining assumptions underlying Newtonian physics. It would eventually become the paradigmatic illustration of Einstein's general theory of relativity. On the other hand, the solution that Max Planck discovered in 1900 to the black-body radiation problem - namely that the electromagnetic emissions of a heated black-body are best modeled by a probalistic rather than a strictly deterministic function - also violated aspects of the Newtonian outlook, and came to illustrate the fundamental principle of quantum physics.
Both philosophers and scientists scrambled to understand what
had happened. How could they have been so very wrong about the
physical nature of the universe? How had their conservative, tough-minded
empiricist views about the methods for the accumulation of knowledge
failed them so completely? Believing that they had been not vigilant
enough in their drive to expunge all metaphysics from their scientific
methods, they redoubted their efforts to remove all assumptions
from their theories which were not explicitly empirically
1.2 Percy Bridgman and Operational Attitude
In 1927 Percy Bridgman, an eminent high-pressure physicist who would win the Nobel prize in 1946, published The Logic of Modern Physics. In it he proposed operational analysis as a check against the kinds of mistakes which, it seemed, had led to the collapse of Newtonian physics. Bridgman was not the first to emphasize the importance of operational analysis, nor did he claim any such priority. Sir Arthur Eddington (1920) had discussed similar notions, and pragmatic philosophers, most notably C.S. Peirce (1878/1955), had also advanced related solutions to the problems of ontology. Bridgman's formulation, however, became the most influential [p. 294] by far. Strangely, though, it was destined to be embraced far more enthusiastically by psychologists than by the physicists for whom it was intended. Its basic thrust was to eradicate all abstract concepts by tying them to the specific operations by which they are measured. In the words of Bridgman, 'we mean by any concept nothing more than a set of operations; the concept is synonymous with the corresponding set of operations' (1927, p. 5, original italics).
For example, Bridgman argued that the concept of length has no meaning in the abstract. Length is measured by various methods, or operations: by ruler, trigonometric triangulation, radar, etc. Each of these methods, according to Bridgman, represents a different sort of length, conceptually. Consequently, there were said to be as many 'lengths' as there are ways of measuring length: ruler length, triangular length, radar length, etc. Each one of these depends upon a different set of assumptions. Among other things, ruler length depends on the ruler not changing its size as it is moved from one point in space to another and as it travels from one point in time to another. Triangular length depends upon additional assumptions, not the least of which is that space is Euclidean in nature. Radar length, in turn, depends on further assumptions such as that electromagnetic waves move at an invariant velocity and in straight lines. Bridgman argued that each of these lengths cannot be proven to give the same result and, in fact, that the very notion of length breaks down at the extremes of the continuum. For extremely large interstellar distances, it becomes confounded with the relativistic nature of space and time. For extremely small subatomic distances, it becomes entangled with the most miniscule aspects of optics, electromagnetic field theory and (ironically) other highly theoretical notions.
It is essential to understand that Bridgman envisioned operations as replacements for the metaphysical concepts which he believed had caused the downfall of Newtonian physics. At the very beginning of his book Bridgman cited an example of such a 'metaphysical error' directly from Newton's Principia:
I do not define Time, Space, Place or Motion, as being well known to all. Only I must observe that the vulgar conceive those quantities under no other notion but from the relation they bear to sensible objects....( I ) Absolute, True, and Mathematical Time, of itself, and from its own nature flows equably without regard to anything external, and by another name is called Duration. (p. 4)
It is important to note the opposition of Newton's and Bridgman's positions. Newton asserted that time is a thing, in and of itself, which must be attached to events which take time only by those who are incapable of understanding its 'mathematical' and 'absolute' nature. By contrast, Bridg- [p. 295] man embraced the 'vulgar', asserting that time has no reality at all apart from its actual measurement. He wrote of Newton's conceptualization:
There is no assurance whatever that there exists in nature anything with properties like those assumed in [Newton's] definition, and physics, when reduced to concepts of this character, becomes as purely an abstract science and as far removed from reality as the abstract geometry of the mathematician, built on postulates. (pp. 4-5)
The reference to geometry was no accident. In geometry, a revolution of proportions equal to the Einsteinian in physics had taken place a few decades earlier, initiated by the overthrow of Euclid by Riemann and Lobachevsky.
Bridgman, in his effort to rid science of such 'errors', insisted
that operational analyses are necessary for all basic theoretical
concepts. He, further, went on to outline operationalizations
of space, time, cause, identity, velocity, force, mass, energy,
as well as of concepts from thermodynamics, electricity, relativity
and quantum theory. Concepts which were not amenable to operationalization
he declared to be nonsense. This term was intended to be taken
literally - non-sensation - but the eventual pejorative overtones
were, and remain, unmistakable.
1.3 Early Criticisms of Operational Analysis
Although the appeal of Bridgman's general position was widely acknowledged, its specifics were criticized almost immediately. L. J. Russell (1928) noted that if one were to consider each different operation as a strictly different concept, instances where different operations, like measuring length with a ruler and by triangulation, give the same result would have no real significance; no more than would be attached to a thermometer and a ruler both reading '37` when applied, respectively, to a person's mouth and chest. The same would hold for a person measuring length with two different rulers, and for two different people using the same ruler, and for one person using the same ruler at different places, or even at different times! Likewise, one should feel no unease at different operations traditionally thought to measure the same concept giving utterly different results if there is no underlying property being measured.
This tendency of operational analysis to turn each individual act of measurement into a concept in its own right came to be seen as one of its major flaws. The idea that objects have independent properties which people merely record is very strongly entrenched in people's notions of the world, and operational analysis, taken as its word, repudiated that belief. Even Bridgman betrayed an underlying belief in abstract notions by distinguishing between 'better' and 'worse' operations. For instance, most people would agree that the measurement of time by means of [p. 296] an electronic digital watch is better than that by means of a spring-powered watch. Such a statement has no meaning, however, unless an abstract time, beyond its measurement by particular devices, is postulated in advance.
Over the next few decades, operational analysis underwent many transformations. Bridgman softened his position somewhat with regard to the admissibility of theoretical constructs in light of the criticism of Russell and others (Bridgman, 1938, 1954/1961; see also Schlesinger, 1967). The logical positivists endorsed many of Bridgman's ideas after Herbert Feigl, a member of the Vienna Circle, spent a sabbatical with Bridgman in 1930. They later rejected Bridgman's analysis, however, as an ultimately unworkable oversimplification of the extremely intricate problem of meaning (Carnap, 1936-1937/1953, 1939, 1956, 1966; Hempel, 1952, 1954/1961, 1964, 1966).
The distinction is important, however, because operationism has often, erroneously, been taken to be strongly akin to, or even identical with, logical positivism (see, e.g., Langfeld, 1945; Pratt, 1939). The logical positivists, however, fundamentally split with Bridgman over two issues in the philosophy of science. One was the issue of the social or public nature of science. The logical positivists insisted that all scientific data must be public where Bridgman (1940, 1945) contended that science is essentially private, depending upon the individual's own perception of objects and events. This is a far cry from the position of the behaviorists, who, thinking it the 'operational' thing to do, often denied the importance, or even existence, of individual experiences.
The second issue which ultimately distinguished logical positivism from operationism, and one which directly bears on the current discussion, concerned the need for explicit definition of terms in science. As early as the mid-1930s the logical positivists were beginning to realize the difficulties entailed by explicit definitions such as those provided by the operationist strategy. First of all, no scientific term can ever be completely defined operationally if there are potentially infinite instances of that which is picked out by the term. This is the realization which led Carnap to replace complete definition with partial reduction of scientific terms (1936, cited in Martin, 1967) and verification with confirmation (1936-1937/1953). Secondly, the necessary incompleteness of such definitions, far from being an unavoidable evil, is itself the very driving force behind scientific research. If terms did not have this 'openness of meaning', as Hempel (1952, p. 29) put it, there would simply be nothing left to discover - all 'legitimate' scientific terms would just be defined in terms of what is already known.
Nevertheless, psychologists still frequently turned to what they
took to be operationism in order to justify some of their more
arcane methodological practices. This dependency continued long
after the difficulties with [p. 297] operational analysis had
been enunciated by the logical positivists as well as by other
philosophers and scientists. It was this mistake which predisposed
psychology to much of the confusion which reigned after the fall
of Hullian theory in the 1950s. Although the main tenets of operationism
have long since been rejected by virtually every serious philosopher
(see, e.g., Carnap, 1936-1937/1953; Frank, 1961; Hempel, 1952),
its powerful terminology has maintained a strong grip on research
psychology to the present day.
2. Behavioral Psychology, 1930-1944
Many psychologists in the early 1930s, particularly those who were in the market for a respectable philosophy of science on which to hang the increasingly popular school of behaviorism, welcomed Bridgman's operational analysis with open arms. Strangely, it took the logical positivist Herbert Feigl, who arrived at Harvard in 1930, to bring the operational attitude to the attention of Bridgman's Harvard colleagues in the psychology department: E.G. Boring and his students, B.F. Skinner and S.S. Stevens. By 1935, the operational attitude, to which Bridgman had entreated physicists to adhere, was being taken by many psychologists to be a full-blown philosophy of science which they called operationism - a term repeatedly rejected by Bridgman himself (1938, 1954/1961).
Tim Rogers (1989) has argued that the seeds of operational psychology go back as far as E.G. Boring's (1923) popular article in The New Republic on intelligence tests. Although there are undoubtedly elements of what psychologists would ultimately take to be operationism in Boring's pronouncement that 'intelligence is what the tests test' (p. 35), there were still significant differences between what Boring and Bridgman advocated. The first mentions of Bridgman and the term 'operationism' in the psychological literature came in two brief notes, one by Stevens (1935a) and the other by Boring (1936), on the applications of operationism to psychology in the American Journal of Psychology. Stevens (1935b) also published a full article in the Psychological Review. Another major psychologist to endorse operationism early on was Edward Tolman, who presented a paper on 'operational behaviorism' at the University of Southern California (1936/1951). He also published a paper entitled 'An Operational Analysis of "Demands"' in the logical positivistic philosophical journal Erkenntnis (Tolman, 1936).
These articles were not without their critics (see, e.g., McGeogh,
1937) but many psychologists were converting to 'operationism'
and soon followed suit, publishing statements of their own beliefs.
The most extensive of these was Carroll C. Pratt's (1939) The
Logic of Modern Psychology (note the similarity to the title
of Bridgman's book). Also, Stevens (1939) [p. 298] published
an extended paper which has come to be generally regarded as the
psychologist's operationist manifesto, 'Psychology and the Science
of Science', in the Psychological Bulletin. Operationism
quickly became the brand of empiricism most widely endorsed
by psychologists. Several of these early writings deserve closer
examination. It is to Tolman's intellectual development that I
2.1 Edward C. Tolman
Tolman's first acquaintance with the operational attitude may have come in 1931 when Moritz Schlick, founder of the Vienna Circle, came to lecture at Berkeley as a visiting professor. While there he met Tolman and invited him to visit Vienna. Tolman accepted and traveled to Austria in 1933, having just completed his Purposive Behavior in Animals and Men (1932). Soon after Tolman's return from Austria in 1934, he read Bridgman's book and enthusiastically joined the ranks of operational psychologists, changing the name of his purposive behaviorism to operational behaviorism (1936).
As mentioned above, there were some important differences between the philosophy of science which the new generation of psychologists were so whole-heartedly embracing and the notions that Bridgman had put forth only a few years before. Those differences are perhaps best exemplified in Tolman's work. Whereas Bridgman had fought to abolish metaphysical concepts and replace them with operations, Tolman's theoretical statements implied that he believed the states of mind he invoked actually existed. Behaviors were taken to be the result of cognitive activities rather than operational redefinitions of the alleged cognitions themselves, as Bridgman would have had it.
In contrast to this, my assessment, Tolman in the 1930s insisted that his use of terms like 'cognition', 'demand' and 'purpose' did not make reference to mental entities but were only 'functional definitions'; that the terms themselves were 'generic' and 'convenient' labels for behavior-gestalts (1932). However, it is difficult to justify Tolman's use of such mentally loaded terms as 'purpose' and 'cognition' if he wished to designate only behavior-gestalts, as he claimed. Although it might be possible usefully to define 'demands' behaviorally, there is no conceivable way to make sense of his crucial concept of behavior-adjustments without asserting the reality of private mental states. Of this concept he wrote:
Behavior-adjustments constitute our behavioristic substitute for, or definition of, what the mentalists would call conscious awareness and ideas. They are unique organic events which may on certain occasions occur in an organism as a substitute, or surrogate, for actual behavior. And they function to produce some sort of modifications or improvements in what were the organism's initially aroused immanent determinants, such [p. 299] that his final behavior, corresponding to these new modified immanent determinants, is different from what it otherwise would have been. (1932, p. 20, italics added)
There is, or course, no behavioral operationalization here at all. Tolman is simply saying, cryptic though he may be, that a strictly behavioristic theory cannot predict behavior as well as might be hoped, and that mental processes, albeit with an adequately behavioral label, must be invoked. If one is to designate oneself a thoroughgoing behaviorist, however, there can be no 'substitute, or surrogate, for actual behavior'.
By the middle of the 1930s, Tolman (1936/1951, 1936) dropped even the pretense of strict behavioral redefinition of mentalistic terms and introduced the phrase 'intervening variable' to refer to those traditional mental concepts which he was striving to operationalize. He asserted, for instance, that the 'food-demand' could be operationally defined by withholding food from a rat for a given number of hours and then seeing how many times it would run across an electrified grid to get food during a specific period of time. The relation between hours of food-deprivation and grid-crossing frequency could then be plotted and:
. . . thereafter, whenever we have given values of Mf ['maintenance schedule': hours of food-deprivation] and Sf ['environmental stimulus objects': electric shock and food], we can look them up on this function and discover the corresponding values for If - the demand for food - even though under these other conditions this demand may no longer betray itself simply and directly in any given behavior. (1936, p. 385)
One must wonder about the predictive utility of knowing how many times a rat would run across an electrified grid in assessing its hunger later under different circumstances. It does not seem to be a situation which would generalize well. To begin with, Tolman was not measuring some 'pure' food-demand at all but a complex interaction between bodily need and tolerance of electric shock. Second, if a purely empirical operational definition of hunger is wanted, hours of food-deprivation is probably a fairly good one. There is no need to find a functional relationship between it and frequency of grid-crossing unless one's real interest is in some internal process. He openly confessed this to be true only near the end of his career when he wrote: 'my own particular brand of intervening variables were admitted to come primarily from my own phenomenology. Thus Köhler's designation of me as a cryptophenomenologist was probably correct' (1959, p. 94, emphasis added).
Finally, if it is admitted that internal processes really are the primary topics of interest, then Tolman's procedure must be considered a poor one because, as he reported himself, 'Bpf [number of grid crossings] increases with time since feeding up to 48 hours without food and remains at approximately the same maximum from that to 96 hours without food, [p. 300] after which it drops again' (1937, p. 385). Therefore, if the number of crossings is to be considered some direct external expression of hunger, we are led to believe that hunger does not increase between 48 and 96 hours and then begins to spontaneously relieve itself! This is nonsense. Clearly, the rat reaches the maximum of its running abilities, not its hunger, after 48 hours, and by the time 96 hours have past it begins to be affected by hunger-induced fatigue; the hunger itself does not subside, as Tolman's argument (but certainly not Tolman himself!) would suggest.
The philosophical point at issue here bears emphasis. Whereas Bridgman offered operations as replacements for the metaphysical concepts which supposedly had led to the crisis in physics, Tolman took operations to measure expressions of those metaphysical concepts which similarly bedeviled psychology. Tolman, in effect, turned operationism inside-out. Where Bridgman sought to rid science of metaphysical concepts, Tolman sought to legitimize them by attaching them to related physical operations. This inversion of operationism would prove to be crucial to the theoretical path followed by psychology through the next few decades.
It has been suggested to me by a reviewer that perhaps this transformation rendered operationism immune to the problems which had plagued Bridgman's formulation of it. There is a superficial sense in which this is true. If, for instance, blood pressure is taken to be a symptom of anger rather than its definition, and the measurement of blood pressure an indirect measurement of anger, then one need no longer worry about an infinite proliferation of angers nor about what constitutes 'better' or 'worse' operationalizations of anger. The infinite proliferation of operations become just infinite possible measurements of one and the same anger, and the operationalization which is 'best' is just the one which correlates most highly with anger itself. There is a deep problem here, however. This is a retreat to exactly the same situation which had held sway before Percy Bridgman and operationism came along in the first place. They are not really operational definitions at all any more. They are more like 'indirect measurement operations' and they suffer from precisely the problems that Bridgman had attempted to address: what ontological sense are you to make of an entity which, in principle, defies observation? Bridgman said you eliminate it in favor of its measurement operation. Tolman said you eliminate it in favor of its behavioral expression (which is not really the same thing), but, more importantly, his theory implied that you continue to (quietly) believe it exists, and do the best you can with the indirect measurements you can get.
Tolman was, by no means, the only psychologist to interpret operationism in this way. His model became a rallying-point for those who wanted to upgrade the scientific reputation of psychology but not at the cost of virtually every traditional concept in the field. Under Tolman's analysis one could maintain that people have drives, goals and purposes, and make [p. 301] conscious decisions in order better to achieve those aims while simultaneously embracing behaviorism and the scientific legitimacy which it conferred in the 1930s. The establishment of such a position was a very desirable thing for many psychologists who believed that rigorous scientific methodology would bring a rapid increase in the rate at which psychology would progress, but could not imagine such progress being possible in the absence of the mental concepts which had been the bread and butter of psychology since before the time of Plato.
Not all psychologists were in agreement with Tolman, however. Skinner opposed Tolman's brand of operational behaviorism from the start. In his seminal Behavior of Organisms (1938) he wrote that the time spent by Tolman and others translating 'vernacular terms' into 'scientific terms' was time spent unwisely; that the science of behavior:
. . . must not take over without careful consideration the [conceptual] schemes which underlie popular speech. The vernacular is clumsy and obese; its terms overlap each other, draw unnecessary or unreal distinctions, and are far from being the most convenient in dealing with data. (p. 7)
Whether he recognized the philosophical transmutation which Tolman's
position entailed, or whether he opposed Tolman purely on the
basis of his own metaphysic - the outright denial of the existence
of mental processes - is a matter of speculation. Regardless of
his motives, however, Skinner got operationism right and would
continue to argue vociferously against Tolman's - and later Hull's
- neobehaviorism, reaching the height of his influence in the
mid-1950s when it became apparent to the psychological community
at large that the models of behavior put forward by both Tolman
and Hull were fatally flawed (see Baars, 1986, for an excellent
2.2 Stanley S. Stevens
By contrast with many accounts of operational analysis offered by psychologists in the 1930s, S.S. Stevens' 'Psychology and the Science of Science' (1939) is outstanding for its clarity and sophistication. The article is a primer of operational analysis and logical positivism which psychologists might still do well to read. It includes a brief account of Bridgman's work, some notes about the psychologists who had attempted operational analysis in their research up to that time, a set of general principles of logical positivistic science, and common misconceptions about operationism.
Stevens' work was not just a psychological rewrite of The Logic of Modern Physics. In addition to outlining the general position and dealing with recent criticism of the method and its applications to psychology, he offered the interesting proposal that the fundamental operation is discrimi- [p. 302] nation. Obviously, this proposal was tied to his well-known work in psychophysics. It went beyond that, however. Bridgman had not established any kind of hierarchy of operations; all were considered relatively equal. Stevens argued, however, that operations stood in hierarchical relation to each other, and where disagreement occurred a more fundamental or basic operation was to be appealed to. For instance, if two individuals cannot agree on whether the behavior of a third person is angry or not, perhaps they can agree on whether it is violent. It not, then perhaps they can at least agree on whether it is swift and sudden, and so on. At the most basic level, they must at least be able to agree on whether any movement can be discriminated at all. Otherwise, there is no common basis for science. Stevens did not, however, assert that all behavior must be reduced to the most basic level. 'Agreement is usually reached in practice', he wrote, 'before these most elementary operations are appealed to' (1939, p. 228).
In some ways, Stevens' work was more comprehensive than even Bridgman's had been. He attempted to bring the philosophy of the Vienna Circle home to a skeptical crowd of lingering old-style positivistic psychologists who had been weaned on the popular but philosophically naive positions of John Watson. He discussed the work of various well-known psychologists of the time who were themselves engaged in incorporating the new philosophy of science into their work. Among these, he mentioned Tolman but remained notably agnostic on whether Tolman's work was to be considered a success from an operational point of view (1939, p. 226).
Stevens proved to be, by far, the most philosophically knowledgeable
of the scientific psychologists who were adopting operationism.
Perhaps for this very reason, he was also the least well understood.
Among today's psychology students, Stevens, if his name is recognized
at all, is better known for his psychophysical power law than
for bringing contemporary empirical philosophy of science to psychology.
Tolman's work, on the other hand, was widely celebrated and studied.
Thus, the misconceptions Tolman had about operationism were destined
to be continued in the research of many important psychologists
2.3 Clark L. Hull
The most prominent purveyor of those misconceptions was Clark Hull. Hull was something of a late-comer to operationism. In 1930 his position seems to have been most indebted to the thought of Thorndike and Watson. There was no mention of any philosophers of science or operationists. By 1935, he had become somewhat more sophisticated philosophically but the type of science he then endorsed was far more beholden to the writings of 19th-century positivists - like Ernst Mach, W.K. Clifford, Karl Pearson and Hermann von Helmholtz - than to the more recent develop- [p. 303] ments in Germany, Austria and at Harvard. Hull himself wrote of his scientific principles:
There is nothing either radical or new in the above criteria of sound scientific theory; on the contrary the program is conservative and respectable to an eminent degree. Indeed, it has been accepted in science for at least two hundred years. Our purpose is mainly to put into practice what we, with the other sciences, have known for a very long time. (1935, p. 497).
There was no mention of Bridgman; in fact his statements regarding scientific definition lead one to believe he was not completely familiar with operational analysis. Neither was there any mention of Tolman's work, apart from a passing reference to 'sign-gestalts', or the methodology that Tolman was adopting (and adapting) from contemporary philosophy of science.
The year 1940 saw the publication of Hull's influential treatise on method, Mathematico-deductive Theory of Rote Learning: A Study in Scientific Methodology. It seems that by this time Hull's grasp of philosophy of science had become more sophisticated still. Interestingly, though, the philosopher to whom he adverted most often was John Dewey. By virtue of Dewey's pragmatist influence, Hull outlined a sort of operational analysis of his own, but one couched not at all in terms common to his time. Most notably absent is any reference to the increasingly fervent debate about operationism current in psychology at the time, or to any of its main players. There is no mention of Boring, Skinner, Stevens or Tolman. It seems incredible that Hull, at Yale, could have missed what was going on in the journals of the time, much less only 100 miles away at Harvard. More likely, he considered arguments about meaning and the intricacies involved in the determination of meaning to be far less important than the actual practice of science, an attitude strongly reminiscent of the 19th -century positivists.
Three years later, Hull published Principles of Behavior (1943). This book was far more accessible than the work which had come out just a few years before and probably marks the beginning of the period of Hull's greatest influence on North American psychology. Hull declared his orientation to be closely allied with Tolman's (1943, p. 31). Accordingly, he not only echoed but amplified some of the advantages, as well as the drawbacks, of Tolman's position.
Like Tolman, Hull strove to 'objectify' hypothetical intervening variables, although the theoretical core of Hull's theory was 'drive' rather than 'demand' or 'purpose'. By 1943, Hull had discovered the work of Bridgman and, like Tolman, explicitly attempted to employ operational definitions from which the unobservable drives could presumably be inferred. It seems, however, that he misread the significance of Bridgman's work even [p. 304] more grossly than had Tolman. It is worth quoting Hull rather extensively to illustrate his point:
In 1938 Bridgman, a physicist whose chief research activities have been concerned with the empirical determination of various physical phenomena under very great pressures, wrote a book [The Logic of Modern Physics] in which he made an acute examination of the use of various concepts in current physical theory, particularly those representing intervening variables. The cure which he recommended for such abuses as he found was the scrupulous recognition of the operations carried out by the experimentalists as a means to the making of observations and measurements of the observable events. This, as we saw above, has special significance for the science of behavior, which is so prone to the subjective use of intervening variables. Quite naturally and properly, Bridgman's work has impressed a great number of psychologists. Unfortunately his emphasis upon the operations which are the means whereby the observations and measurements in question become possible has led many psychologists to mistake the means for the end. The point here to be emphasized is that while observations must be considered in the context of the operations which make them possible, the central factor in the situation is what is observed. The moral of Bridgman's treatise is that the intervening variable is never directly observed but is an inference based on the observation of something else, and that the inference is critically dependent upon the experimental manipulations (operations) which lead to the observations. An emphasis on operations which ignores the central importance of the dependent observations completely misses the virtue of what is coming to be known as operationism. (p. 30, original italics)
Many errors in this passage require highlighting. First, Hull's
date is 11 years too late: The Logic of Modern Physics was
first published in 1927. Bridgman did publish an article on operational
analysis in 1938, a response to a critique by R.B. Lindsay (1937),
but this cannot be the object of Hull's comments. Second, the
term 'intervening variable' never once appeared in Bridgman's
work. His operational analyses were directed at concepts for
which well-established methods of measurement had long since been
developed and were now said to constitute individual and distinct
concepts themselves. Third, the 'moral of Bridgman's treatise'
was nothing like Hull's contention that the 'intervening variable
... is an inference based on the observations', but, rather, that
the concept is synonymous with the corresponding set of operations,
a very different notion indeed. Hull would have it that the observation
of a number of operations theoretically purported to be related
to one another lead one to infer an underlying intervening variable
from which they all stem. It will be remembered,
however, that under Bridgman's original conceptualization each
operation establishes a new concept and all unobservables are
tossed out the window, or so it was hoped. Although Bridgman's
original statements were taken literally by almost no serious
philosopher as late as 1940, there is little [p. 305] evidence
in the psychological literature that any prominent psychologists
were incorporating the developments that philosophers of science
were advancing at that time. They seem to have simply missed the
3. Behavioral Psychology, 1945-1960
3.1 The Symposium of 1945
Thus far, it has been argued that the various psychologists and psychological camps which had nominally adopted operationism were far from agreement on exactly what operationism was and what it implied. At no point did the diversity of opinion become more evident than in a 1945 symposium on the topic sponsored by the Psychological Review. The journal's editor, Herbert S. Langfeld, solicited statements from Edwin G. Boring, Percy Bridgman, Herbert Feigl, Harold E. Israel, Carroll Pratt and B.F. Skinner on several of the most fundamental issues facing the proponents of operational analysis. The set of questions to which the contributors were asked to respond was as follows:
1. (a) What is the purpose of operational definitions? When are they called for?
(b) Logically, operational definitions could form an infinite regress. How is this regress limited in scientific practice?
2. When the same construct is defined by two different operations, should it be said that there are really two constructs?
3. (a) Are hypothetical operations which are physically impossible with present available techniques of scientific use?
(b) Is there a use for hypothetical operations that would define constructs which are presently non-existent (e.g. a color we cannot see)?
(c) Is there a use for hypothetical operations which could never be performed (e.g. the notion of infinity)?
4. Is experience a proper construct for operational definition?
5. Are there scientifically good and bad operations, and how are operations evaluated if they differ in value?
6. Is operationism more than a renewed and refined emphasis on the experimental method (as understood already by Galileo, if not Archimedes)?
7. Must operationists in psychology relegate theorizing of all sorts to the limbo of metaphysics?
8. What possible meaning is there in talking about improving or revising tests if there are no criteria outside the chosen test method?
9. Are all scientifically legitimate definitions operational in character?
10. What is a definition, operational or otherwise?
11. Can a phenomenon be identified or its properties be defined in terms of the events (operations) which are effective to produce, or occur as results of, the phenomenon?
|1a) Purpose of operational definitions||Precision and unification of science||Precision||Eliminate obscurity, ambiguity, vagueness; adapt term to wider context; add new term||--||Heuristic value||Precision|
|1b) Do they form an infinite regress?||Regress ends when agreement is reached||Not infinite; semi-convergent||Not infinite; ends when definition is 'ostensive'||--||--||--|
|2) Can different operations define the same construct?||Only when the equivalence of the operations is established||Never safe to assume equivalence||Established empirical laws give rules of equivalence||Never; operationism leads to multiplicity of concepts||--||Only if the operations result in the same response|
|3a) Can operations which are now impracticable be useful?||Yes||Yes||Yes||--||--||--|
|3b) Are operations which define non-existent constructs useful?||Yes||?||?||--||--||--|
|3c) Can operations which are impossible in principle be useful?||Yes||Yes||Yes||--||--||--|
|4) Is 'experience' a proper construct for operational definition?||Yes||Answerable by experiment only||No||--||No||--|
|5) Are there 'good' and 'bad' operations?||Yes||'Useful' and 'non-useful' are preferable terms||Yes(?)||'Operation' is itself ill-defined||--||--|
|6) Is operationism more than a renewed emphasis on experimental method?||Yes||Yes||No||--||--||Yes|
|7) Does operationism relegate all theorizing to metaphysics?||Yes(?)||No||No||--||All theory is tautological||--|
|8) If the operation defines a construct, how can we speak of 'improving' an operation (e.g. IQ test)?||By establishment of equivalence to something else||Only the start of a process of spiral approximation||Only the start of a 'long labor of adjustment and redefinition'||--||--||--|
|9) Must all scientifically legitimate definitions be operational?||Yes||Yes||No||--||--||Yes|
|10) What is a definition?||A statement of equivalence||Always operational||A rule concerning the use of a symbol||--||--||The science of verbal behavior of scientists is not yet developed enough to say|
|11) Can a concept be defined in terms of the operations which produce it or result from some hypothetical phenomenon?||If correlation between the antecedent and consequent operation is found||Perhaps, but only useful in initial stages, if at all||Yes, initially, but the concept should be well-enough developed that at least two operational definitions are known||--||--||--|
Consensus among the various contributors on these questions was sparse. A synopsis of their responses is offered in Table 1. More striking than the amount of literal disagreement, however, is the wide diversity in the tone and style of their responses. It is, in fact, difficult to ascertain exactly how much concurrence there was among the participants because each symposium paper often reads as though the participants were simply writing about different things. It is clear, however, that the adoption of operationism had not, as per its early promise, led to the rise of a united scientific psychology. Boring attempted to put the best face on the evident disunity by writing: 'this symposium has strengthened my faith [!?] in operationism immeasurably because of the essential agreement that runs through accounts that diverge in detail' (1945, p. 281). The truth was that much of the symposium consisted of the participants excoriating each other for being in error, 'off topic' or just plain nonsensical.
Boring emphasized the unity of science, the mandatory use of 'physicalist' language and the publicity of all 'scientific' phenomena: 'Science does not consider private data' (1945, p. 244). Bridgman, by contrast, argued for the inherent privacy of 'the most important part of science' (p. 281). The endeavor to treat private and public phenomena (e.g. feeling the pain of a toothache vs wincing and moaning) as equivalent, either because one regards their apparent differences as merely apparent or because one believes the difference to be unimportant, he regarded as 'opposed to the entire spirit of the operational approach' (p. 282). In fact, Bridgman ultimately rejected radical behaviorism on this basis.
Feigl's position was more or less the orthodox logical positivism of the day, complete with much talk about 'meaningfulness' and repudiations of 'metaphysics' (used in a somewhat pejorative sense). Whereas Boring and Bridgman had both conceded the possibility of operationalizing the concept 'experience', Feigl rejected experience as inherently unscientific. Pratt, as well, rejected as impossible the prospect of making experience scientifically acceptable by operationalization. Paradoxically, however, he agreed with Bridgman's view of the scientific data, writing that the 'initial data of behaviorism are no more public than are the data of introspection . . . . Both reports intend experiences which are equally private' (1945, p. 263). This did not lead him to regard introspection as a legitimate tool of science, however. 'The use of operationism as a pointer for those whose eyes have been blinded by the dust of naive objectivism', he wrote, may serve a good purpose. The only danger is that the fervent apologists for neo-introspectionism, such as Professors Boring and Stevens, will mistake the pointer for the thing being pointed to' (p. 263). Such perplexing remarks [p. 309] led Boring to remark about Pratt: 'I do not know what to say about him. He directs invective against values that I believe I am prepared to defend, and then he ends up with conclusions that seem perfect to me and beautifully formulated' (p. 278). (Because Harold Israel was included in the 1945 symposium just because he was a strong critic of operationism, I will refrain from commenting on his contribution.)
Skinner's response, however, was perhaps the most astounding. He began with a page of withering attacks on the foundations and practice of operationism, only to conclude that it is, nevertheless, 'a good thing in any science but especially psychology' (1945, p. 271). He went on to argue that 'behaviorism had been . . . nothing more than a thoroughgoing operational analysis of traditional mentalistic concepts' (p. 271). To this, Pratt responded that it 'must come as a surprise not only to psychologists who have used traditional concepts, but also to most behaviorists . . . for it implies that traditional or classical psychology was sound enough in its choice of subject-matter' (p. 288). After that point, however, Skinner's contribution digressed into a discussion of his own idiosyncratic view of psychology; so much so that it prompted Boring to write, 'Skinner is full of his unpublished book and that makes difficulty' (p. 278). One interesting aside is that, contrary to some earlier writings, Skinner here claimed that 'each speaker possesses a small important private world of stimuli' (p. 272). This led him to (wryly?) conclude, contra Boring, that:
...my toothache is just as physical as my typewriter, though not public, and I see no reason why an objective and operational science cannot consider the processes through which a vocabulary descriptive of a toothache is acquired and maintained. It is an amusing bit of irony that, while Boring must confine himself to an account of my external behavior, I am still reasonably interested in what might be called Boring-from-within. (1945, p. 294).
It should be kept in mind that I have explicitly attempted, here, to compare the positions of those who participated in the 1945 symposium. Thus, any appearance of broad agreement on what issues were to be considered relevant may well be an artifact of the exercise itself. As noted above, the disparity of tone and topic makes more detailed comparisons almost impossible.
Along these lines, Rogers (1989) has recently argued that there
were several different 'operationisms' in psychology in the 1930s
and 1940s and that it was legitimate difference of opinion that
led to such disagreements. It is my belief, however, that this
is too charitable a characterization of what was going on at the
time. Not only did psychologists frequently and vociferously do
combat over what exactly counted as operationism. Over the long
haul they just as regularly failed to acknowledge the problems
which Carnap, Hempel and Bridgman himself, among others, had pointed
[p. 310] out. This was the result not merely of scholarly difference
of opinion but of scholarly indolence as well. Nevertheless, the
historical narrative offered by Rogers may well be correct: 'operationism',
rather than starting out as a cause in itself, simply gave psychologists
a name for the standard defense of intelligence testing in the
1920s (namely that intelligence is just what the tests test);
a flag to rally around. Unfortunately, this was not what Bridgman
had in mind when he outlined the operational attitude. No one
ever doubted that length exists and can be measured with a ruler.
The question was about what length, per se, is. By contrast, people
continue to doubt that intelligence is a measurable thing at
all; much less a thing which can be measured by paper-and-pencil
tests. If psychologists indeed prescribed operationism to cure
this ill, they had the wrong answer to the wrong problem.
3.2 Koch's Repudiation of Operationism
By the 1950s, even Bridgman, who had never been comfortable with the scholastic overtones his ideas had acquired, repudiated operationism. He wrote in a 1954 symposium in Scientific Monthly: 'I feel as if I have created a Frankenstein, which has certainly gotten away from me. I abhor the word operationalism or operationism which seems to imply a dogma, or at least a thesis of some kind. The thing I have envisaged is too simple to be dignified by so pretentious a name' (1954/1961, p. 76).
An important observer and chronicler of the rise and fall of operationism was Sigmund Koch. Having studied under Feigl in the 1940s, Koch had initially been enthusiastic about the operationist/behavioral movement, terming it 'the new methodological renaissance' (1941). By the 1950s, however, he was less enamored of its achievements. In 1951 he published a damning critique of motivational psychology (1951a) and an unflattering appraisal of the state of theoretical psychology at large (1951b).
In 1954 he contributed an extensive analysis of Hull's theoretical work to William Estes' Modern Learning Theory. He concluded that, while Hull's efforts had been instructive, 'in the present state of our ignorance, no one can seriously believe that a comprehensive, quantitative hypothetico-deductive theory of behavior is yet possible' (p. 159). According to Koch, the primary failure of Hull's theory was that, contrary to his own demand, Hull neither demonstrated 'explicit and univocal linkages' among independent, intervening and dependent variables nor did he securely anchor independent and dependent variables to their 'operational symptoms' (p. 160). Note here that Koch provisionally accepted the Tolman/Hull rewrite of operational analysis and that even under their own understanding of operationism their theories failed. Such criticisms signaled the passing of Hull's drive theory into the history of psychology and the arrival of Koch as a major player in theoretical psychology.
[p. 311] In 1959 Koch completed work on his multi-volume Psychology: A Study of a Science. The study consisted largely of thousands of pages of personal testimonials from the most prominent psychologists of the era about their methods and conclusions. Many of them had once been among the strongest advocates of the operationist strategy and almost all had ultimately come to doubt its efficacy: Edward Tolman, Egon Brunswick, R.B. Cattell, Edwin Guthrie and Neal Miller, to name just a few. Koch came within a breath of saying the previous 30 years' work had been a failure, a mere mirage of science spotted on the horizon.
3.3 The Tenacity of Operationism
Contrary perhaps to expectation, these events did not kill support for operationism in psychology. Certain of its vestiges seem to have become implicit and unquestioned imperatives about how psychologists should conduct research. So engrained in psychological research method did operationism become in the days of Tolman and Hull that psychologists seemed not to take notice when virtually every major philosopher of science, including Bridgman himself, rejected it during the 1940s and 1950s. It is well worth noting that the famous attempts to salvage operationism (though they are not usually billed this way) by MacCorquodale and Meehl (1948) and Cronbach and Meehl (1955), while admirable efforts to grapple with a crucial problem which psychology faced at the time, really did little, from a philosophical standpoint, to repeal the inevitable. As Gergen (1982) has noted, they were based on outdated positivistic assumptions about the relationship between words and things which are now widely recognized to be untenable.
Nevertheless, even today virtually no research methodology text is without its fairly extensive but uncritical treatment of operational definitions. Underwood (1957) devoted an entire chapter on the topic in his famous research design text. So fundamental did he regard the question of operationism that he wrote: 'to ask such a question is to ask whether one accepts science as a technique for understanding the laws of nature' (p. 52).
Although the treatment was not quite so extensive, writers of research texts during the 1960s and 1970s continued to rank operational definitions among the top requirements of scientific method. Bachrach (1965) wrote: 'fundamental to all scientific method is the operational definition' (p. 74). Lyons (1965) declared operational definitions to be 'of fundamental importance to modern psychology' (p. 16). Johnson and Solso (1971) called them a 'must' (p. 34). Myers (1976) contended that operational definitions make scientific terminology 'objective and precise' (p. 56). Reaching back even further into the history of operationism, Kerlinger (1979) insisted that 'an operational definition assigns meaning to a construct or variable' (p. 41).
[p. 312] These views did not wane perceptibly even in the 1980s. The imperative tone remained as strong as ever. Sommer and Sommer (1980) held that 'the concepts included in the hypothesis must be operationally defined' (p. 54). Neele and Liebert (1980) argued that operationism 'has served behavioral and social research in very good stead', and that 'moving away from operational definitions begins to erode the solidarity[?] of meaning of a theoretical term and thus invites theoretical and conceptual invalidity' (pp. 256-257). Bachrach (1981) repeated his claim that operational definitions are 'fundamental' (p. 74). Christensen (1981) wrote that 'terms must be operationally defined' (p. 9). Kidder (1981) stated categorically that 'scientific measurement is accomplished with operational definitions that can be used and repeated by any number of people. That is what makes operational definitions objective' (p. 123). McGuigan (1983) argued that 'by subjecting the [research] problem to the criterion of operational definition of its terms, we render a . . . decision [as to its ultimate solubility], on the basis of which we either continue or abandon our research on the question' (p. 30). Drew and Hardman (1985) taught that securing operational definitions 'is an essential step in problem distillation and must precede implementation of the study' (p. 58). Elmes, Kantowitz, and Roediger (1985) called operational definitions 'a crucial component of research' (p. 18). Miller (1987) extolled their 'beneficial impact on psychology', claiming that 'if [mental attributes] are to be studied they must somehow be operationalized' (p. 13). Christensen (1988) again, in a later edition, held that 'we must translate the independent variable into concrete operational terms' (p. 117), and that 'operational definitions are necessary for scientific communication' (p. 131). Bordens and Abbott (1988) asserted that 'using operational definitions allows you to measure precisely the states of the two variables (IV and DV) in question' (p. 29). Whalen (1989) taught that 'we must develop what is called an "operational" definition for each variable' (p. 28). Even in the present decade, though his enthusiasm was somewhat muted, Ceolican (1990) wrote that 'in search of objectivity, scientists conducting research attempt to operationalize their variables' (p. 18).
Though not by any means a rigorous survey, of some 20 texts on research design which I, more or less blindly, pulled off shelves in two university libraries, the only one which presented anything approaching an adequate history and critique of operationism was Plutchik (1968). The other 19 cited above declared operational definitions to be a central feature of good scientific practice. Of those 19, little or no attention was paid to the significant problems facing operationism in 17 of them.
As recently as 1989, Gregory Kimble has argued for the scientific necessity of operational definitions and intervening variables. Consider the following excepts: 'motivation, attention, and comparator processes require objective definition' (p. 491, original italics). 'Psychology is the science of [p. 313] behavior' (p. 491). 'Inner phenomena like thought, emotion, and ambition are not part of the basic definition [of psychology] because they are not observable. They are concepts, inferences from behavior' (p. 491). The program Kimble advocates is little changed from that espoused during the heyday of neo-behaviorism but careful examination has since shown many of its main tenets to be false or meaningless. Reassuringly, Kimble's assertions did not pass by unchallenged. Rozeboom (1990) criticized his apparently unexamined acceptance of naïve hypothetico-deductivism, calling it 'perniciously vacuous' (p. 555). Green and Powell (1990) questioned Kimble's warrant for legislating inner phenomena out of psychology's basic vocabulary a priori simply for being not directly observable. 'Under this reasoning', they noted, 'subatomic physics is not the study of subatomic particles and events but, rather, of vapor trails and Geiger counter clicks' (p. 557). If this paper has demonstrated anything, it is that assertions as bald as those made by Kimble have little place in late 20th-century psychology.
Thomas Leahey (1980) attempted to put operationism to bed for good with an article in the Journal of Mind and Behavior entitled 'The Myth of Operationism'. He argued that operationism is inherently wedded to a positivist outlook, and that, while little else has come to replace it, positivism is only one of a variety of stances one can take with regard to psychological inquiry. The recent erosion in philosophical discourse of the distinction between statements which can be regarded as 'theoretical' and those which are 'observational' - a breakdown implicit in the work of many perception researchers as well as philosophers - undercuts the very reason that operational analysis was developed in the first place. In his final assault on operationism he wrote:
Operational definition is a myth, a remnant of an obsolete philosophy of science, but a myth that commands the allegiance of most psychologists. . . . But removed from its historical context and stripped of its philosophical justification, operationism became a talisman and 'operational definition' a liturgical phrase. Continued use of the operational liturgy blinds psychologists to the nature of science as a pragmatic struggle of human minds against the facts of experience. (p. 141)
He concluded by comparing present-day 'operational' psychologists to the proverbial psychiatric patient in New York who constantly claps his hands to keep elephants away. When told by his doctor that there are no elephants in New York, the patient responds, 'See, it works!' 'Similarly', Leahey wrote, 'operationism is a myth that seems to work, that offers security, but which deludes psychologists about the nature of science' (p. 141).
Far from putting operationism to rest, Leahey's article stirred up a storm of protest from Howard Kendler (1981, 1983), who claimed that Leahey [p. 314] was 'obsessed' with philosophy and was unable to see that operational definitions 'need not be justified by philosophical analysis' and still have tremendous value from a 'research perspective'. Paradoxically, he also asserted - incorrectly, if the small sample of research design texts surveyed above is any indication at all - that 'discussions of operationism have disappeared from introductory textbooks . . . because contemporary authors do not share the commitment to an operational approach of their predecessors' (1981, p. 332). Leahey attempted to articulate his position further in two later articles (1981, 1983). Unfortunately, Kendler - like a great number of psychologists - failed to understand that all research methods require philosophical justification at some level. The very methods one uses, the very things one looks for, the very criteria by which one 'knows' if one has found 'them', necessarily imply metaphysical positions of one sort or another. If they are not made explicit, then, as noted by Edwin Burtt back in 1932, such positions will be held uncritically and be propagated to others by insinuation rather than direct argument (cited in Leahey, 1983). Such a situation is anything but optimal for the development of understanding.
Astounded at the tenaciousness of operationism in light of the overwhelming arguments against it, Rosenwald (1986) has argued that a number of 'extra-scientific' factors may be responsible for its persistence, particularly in social psychology. Because the social world is often perplexing, social psychologists conduct laboratory research in an effort to reduce the number of factors at work and gain control over those factors which are admitted to a given experimental situation. Operationism, viewed uncritically, holds out the promise of making such simplification and control possible. Typically, limited domain theories are developed and support for them is found in controlled experiments. The ensuing criticism of such research, however, often focuses on the (in-) adequacy of the operationalizing; the subjects, it is often argued, may have interpreted the experimental situation in a way other than that intended by the experimenter. This is followed by a replication of the experiment with a new and allegedly improved operationalization. Another critique comes out, battering the new operationalization, and around we go, the original researcher searching for an invulnerable operationalization and a team of critics perpetually reinterpreting the outcome as having failed to test the theory in question at all.
What they all fail to realize, argues Rosenwald, is that no operationalization will ever be fully adequate: whereas the researcher is busily engaged in the (ultimately futile) attempt to strip pre-theoretic social knowledge away from the experimental situation through the process of operationalization, the critic can always bring such knowledge to bear on the experimental outcome - and as criticism, the knowledge will stick. In Rosenwald's words:
[p. 315] Social or cultural knowledge . . . which is shared by the members of the society and which guides our interpretation of everyday social experience despite being unsystematic and occasionally vague or self contradictory - such knowledge is not only more voluminous than that which we succeed in establishing scientifically, but enjoys a normative privilege. (p. 319, original emphasis)
The scientific result of this process, he went on, is that:
. . . because we wish urgently to gain mastery over pressing human perplexity, we are untiring in the pursuit of adequate operationalizations, and because we are relatively sophisticated about these perplexities [by virtue of our social knowledge], we tend to reject most of the attempted solutions as inadequate. (p. 321)
It seems that nothing less than a complete rewrite of the rules of social research is required. As Rosenwald would have it, the new edition must explicitly include the interpretive powers of the subject, rather than desperately attempt to strip them away. Only then can social psychological research exhibit the external validity which is needed to justify its time and expense.
This may well be true, but I do not think a hermeneutic turn alone will solve the conceptual problems of psychological research generally. What is required is a more sophisticated approach to conceptual analysis in general. Phenomena such as learning, memory, reasoning, perception and emotion can be neither adequately defined in terms of, nor reduced to, a small set of measurement operations. They each have immanent features which are ignored at the researcher's peril. To take just one example, the recently renewed debates about intentionality - a term virtually banned by the behaviorists - are evidence of how essential features cannot simply be defined out of existence. That intentionality itself remains elusive is no warrant for ignoring it. It is a challenge put to all psychologists: 'Until you understand me, you will understand nothing else fully!' The challenge must be met by combination of empirical and intellectual weaponry. One cannot be useful without the other. Although operational definitions might have a role to play in piloting nascent thought about a given phenomenon, they cannot ultimately replace the fruits of hard, rigorous thought. In the words of Immanuel Kant (1781/1965, B76), 'thoughts without content are empty, [sensory] intuitions without concepts are blind'.
 Even Boring, who was presumably one of the converted, described Watson as 'philosophically inept' (1929, p. 494). In 1950 he added that it took E.B. Holt and E.C. Tolman to write a 'constitution' for behaviorism and logical positivism to give it a solid philosophical base (p. 506).
[p. 316]  Although this notion of 'inferring back'
from a number of distinct behaviors to some single underlying
source has been frequently invoked by a number of psychologists,
the logic of the argument is not made explicitly clear. If its
structure is taken to be:
then it is clearly specious because there may be all manner of
alternative explanations of the predicted behavior (fallacy of
affirming the consequent). If, on the other hand, the argument
is taken to be:
the logic is valid but the argument may be unsound because the truth of Premise 1 cannot be demonstrated (problem of induction). Part of the strength of the radical behaviorist position derives from its ability to avoid this problem entirely by hypothesizing no underlying sources of behavior. As with Tolman's work, it is interesting to note that although not fully developed and though he never referred to Carnap or Hempel, Hull seems to have been groping toward something like deductive confirmationism.
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I would like to than John A. Mills, John M. Kennedy, John Vervaeke and the members of the Scarborough College Cognitive Science Colloquium Group for their comments and suggestions concerning earlier drafts of this paper.
Christopher D. Green is completing his PhD in psychology at the University of Toronto. His primary interests are in theoretical cognitive science and the history of psychology. He is currently conducting research on deductive reasoning processes. ADDRESS: Department of Psychology, University of Toronto, 100 St George St, Toronto, Ontario M5S 1A1, Canada.