Great Minds in Management:  The Process of Theory Development
Bob Jensen at Trinity University
Homepage:  http://www.trinity.edu/rjensen
 

In April 2006 I commenced reading a heavy book entitled Great Minds in Management:  The Process of Theory Development, Edited by Ken G. Smith and Michael A. Hitt (Oxford Press, 2006).

The essays are somewhat personalized in terms of how theory development is perceived by each author and how these perceptions changed over time.

Below I will share some of the key quotations as I proceed through this book. The book is somewhat heavy going, so it will take some time to add selected quotations to the list below.

Bob Jensen

"Cornell Theory Center Aids Social Science Researchers," PR Web, June 19, 2006 --- http://www.prweb.com/releases/2006/6/prweb400160.htm

The following "great minds" contributed to this book:

Where did the giant Harvard economist John Kenneth Galbraith fail?

Leaders and the Responsibility of Power

Bob Jensen's threads on accounting theory --- http://www.trinity.edu/rjensen/theory.htm

The Evolution of Social Cognitive Theory
ALBERT BANDURA

PG#19 BANDURA
Fortuitous events got me into psychology and my marital partnership.  I initially planned to study the biological sciences.  I was in a car pool with pre-meds and engineers who enrolled in classes at an unmercifully early hour.  While waiting for my English class I flipped through a course catalogue that happened to be left on a table in the library.  I noticed an introductory psychology course that would serve as an early time filler.  I enrolled in the course and found my future profession.  It was during my graduate school years at the University of Iowa that I met my wife through a fortuitous encounter.  My friend and I were quite late getting to the golf course one Sunday.  We were bumped to an afternoon starting time.  There were two women ahead of us.  They were slowing down.  We were speeding up.  Before long we became a genial foursome.  I met my wife in a sand trap.  Our lives would have taken entirely different courses had I showed up at the early scheduled time.

Some years ago I delivered a presidential address at the Western Psychological Convention on the psychology of chance encounters and life paths (Bandura, 1982).  At the convention the following year, an editor of one of the publishing houses explained that he had entered the lecture hall as it was rapidly filling up and seized an empty chair near the entrance.  In the coming week, he will be marrying the woman who happened to be seated next to him.  With only a momentary change in time of entry, seating constellations would have altered and this intersect would not have occurred.  A marital partnership was, thus, fortuitously formed at a talk devoted to fortuitous determinants of life paths!

Fortuitous influences are ignored in the casual structure of the social sciences even though they play an important role in life courses.  Most fortuitous events leave people untouched, others have some lasting effects, and still others branch people into new trajectories of life.  A science of psychology does not have much to say about the occurrence of fortuitous intersects, except that personal proclivities, the nature of the settings in which one moves, and the types of people who populate those settings make some types of intersects more probable than others.  Fortuitous influences may be unforeseeable, but having occurred, they enter as contributing factors in casual chains in the same way as prearranged ones do.  Psychology can gain the knowledge for predicting the nature, scope, and strength of the impact these encounters will have on human lives.  I took the fortuitous character of life seriously, provided a preliminary conceptual scheme for predicting the psychosocial impact of such events, and specified ways in which people can capitalize agentically on fortuitous opportunities (Bandura, 1982, 1998).

PG.#24 BANDURA
Scientific advances are promoted by two kinds of theories (Nagel, 1961).  One form seeks relations between directly observable events but shies away from the mechanisms subserving the observable events.  The second form focuses on the mechanisms that explain the functional relations between observable events.  The fight over cognitive determinants was not about the legitimacy of inner causes, but about the types of inner determinants that are favored (Bandura, 1996).  For example, operant analysts increasingly place the explanatory burden on determinants inside the organism, namely the implanted history of reinforcements.

PG.#27 BANDURA
Not only are cultures not monolithic entities, but they are no longer insular.  Global connectivity is shrinking cross-cultural uniqueness.  Moreover, people worldwide are becoming increasingly enmeshed in a cyberworld that transcends time, distance, place, and national borders.  In addition, mass transnational influences are homogenizing some aspects of life, polarizing other aspects, and creating a lot of cultural hybridizations fusing elements from diverse cultures.

PG.#29 BANDURA
Controlled field studies that systematically vary psychosocial factors under real-life conditions provide greater ecological validity, but they too are limited in scope.  Finite resources, limits imposed by social systems on what types of interventions they permit, hard to control fluctuations in quality of implementation, and ethical considerations place constraints on controlled field interventions.  Controlled experimentation must, therefore, be supplemented with investigation of naturally produced variations in psychosocial functioning linked to identifiable determinants (Nagel, 1961).  The latter approach is indispensable in the social sciences.

Verification of functional relations requires converging evidence from different research strategies.  Therefore, in the development of social cognitive theory, we have employed controlled laboratory studies, controlled field studies, longitudinal studies, behavior modification of human dysfunctions not producible on ethical grounds, and analyses of functional relations in naturally occurring phenomena.  These studies have included populations of diverse sociodemographic characteristics, multiple analytic methodologies, applied across diverse spheres of functioning in diverse cultural milieus.

PG.#30 BANDURA
It is one thing to generate innovative ideas that hold promise for advancing knowledge, but another to get them published.  The publication process, therefore, warrants brief comment from the trenches.  Researchers have a lot of psychic scar tissue from inevitable skirmishes with journal reviewers.  This presents special problems when there is conceptual inbreeding in editorial boards.  The path to innovative accomplishments is strewn with publication hassles and rejections.

It is not uncommon for authors of scientific classics to experience repeated initial rejection of their work, often with hostile embellishments if it is too discordant with what is in vogue (Companario, 1995).  The intellectual contributions later become the mainstays of the field of study.  For example, John Garcia, who eventually was honored for his fundamental psychological discoveries, was once told by a reviewer of his often-rejected manuscripts that one is no more likely to find the phenomenon he discovered than bird droppings in a cuckoo clock.

Gans and Shepherd (1994) asked leading economists, including Nobel Prize winners, to describe their experiences with the publication process.  Their request brought a cathartic outpouring of accounts of publication troubles, even with seminal contributions.  The publication hassles are an unavoidable but frustrating part of a research enterprise.  The next time you have one of your ideas, prized projects, or manuscripts rejected, do not despair too much.  Take comfort in the fact that those who have gone on to fame have had a rough time.  In his delightful book Rejection, John White (1982) vividly documents that the prominent characteristic of people who achieve success in challenging pursuits in an unshakable sense of efficacy and a firm belief in the worth of what they are doing.  This belief system provides the staying power in the fact of failures, setbacks, and unmerciful rejections.

PG.# 31 BANDURA
There is much talk about the validity of theories, but surprisingly little attention is devoted to their social utility.  For example, if aeronautical scientists developed principles of aerodynamics in wind tunnel tests but were unable to build an aircraft that could fly the value of their theorizing would be called into question.  Theories are predictive and operative tools.  In the final analysis, the evaluation of a scientific enterprise in the social sciences will rest heavily on its social utility.

Image Theory
LEE R. BEACH and TERENCE R. MITCHELL

PG.# 39 BEACH and MITCHELL
This state of affairs elicited two immediate responses from behavioral decision researchers.  The first was to declare decision makers flawed and to insist that they learn to behave as the normative models prescribed.  The impact of this response has been minimal; there is little or no evidence that training in decision theory or decision analytic methods makes one a better decision maker.  The second response was to modify normative theory, usually by retaining the general maximization of expected value framework but adding psychological assumptions that make the theory more predictive of actual decision behavior.  Kahneman and Tversky's Prospect Theory (1979, Tversky and Kahneman, 1992) is the prime example of this response.  By taking into account various biases, the underlying logic of the normative model remained relatively unscathed.

Quite aside from whether observed decision making resembles a gambler behaving as normative theory prescribes, there are two very large logical problems with the gamble analogy itself.  The first is that the expected value of a gamble is the amount that the gambler can expect to win, on average, if he or she plays the gamble repeatedly.  However, it is not at all clear what expected value means for a single gamble; the gambler either wins or loses and the average is irrelevant.  Thus, the gamble analogy may hold if a decision maker makes a series of highly similar decisions, but it probably does not hold for unique decisions.  In fact, in laboratory studies, gamblers treat repeated and unique gambles very differently (Keren and Wagenaar, 1987).  Because decision makers regard the bulk of their decisions as unique, it seems unlikely they would treat many of them like gambles, which makes the analogy inappropriate.  A manager does not approach a major decision with the idea that he or she will get to do this repeatedly and all that matters is that he or she is successful, on average, over the long run.

The second problem with the gamble analogy is that real gamblers doe not get to influence the outcomes of gambles; they place their bet and await the turn of the card or the spin of the wheel.  In personal and organizational decision making, substantial time may elapse between the decision and its outcomes and most of us use this time to do our utmost to influence those outcomes.  We acknowledge that risk abounds, but we do not accept the passive role of a gambler who patiently waits to see if he won or lost. This is why probabilities make so little sense to most people --- they want to use probabilities to describe the overall riskiness of the decision task, but they do not want to attach probabilities to every attribute of each decision alternative. In fact, real world decision makers insist that they try to nullify risk (probability) by working hard to make sure that these things come out well.

PG.# 41 BEACH and MITCHELL Both of us had a history of working with Fred Fiedler.  Among the many contributions Fred has made to organizational theory, one of the most important is the concept of contingency theory.  A contingency theory assumes that behavior is contingent upon the characteristics of the person, the characteristics of the task, and the characteristics of the environment in which the person and the task are embedded.  The theoretical problem is to identify the components of each of these three classes of characteristics.  The empirical problem is to see how the components of these classes of characteristics influence the behavior of interest.

So, based on our introspections about our own decision strategies and on our familiarity with the relevant literature, we began to write a contingency theory of decision strategy selection.  We began with the idea that decision makers have repertories of strategies that range from aided analytic strategies, such as decision matrices and decision trees based on SEU, which usually require the help of a computer and/or a decision analyst: to unaided analytic strategies, such as Simon's (1957) "satisfying rule"; to simple nonanalytic strategies, such as a rule of thumb or asking a friend or consulting a fortune teller.  The expenditure of effort (and, sometimes, money) required to use these strategies decreases from aided analytic to nonanalytic.  Moreover, there are individual differences in the strategies decision makers have in their repertories.

The decision maker's characteristics are knowledge of strategies, ability to use them, and motivation.  The latter is characterized as wanting to expend the least effort compatible with the demands of the decision task, whose characteristics are unfamiliarity, ambiguity, complexity, and instability.  The decision maker and the task are embedded in a decision environment characterized by the irreversibility of the decision, significance, accountability for being correct, and time/money constraints.  The strategy selection mechanism is driven by the decision maker's motivation: Select a strategy by balancing the effort of using it against its potential for producing a desirable outcome.

PG.# 42, 43and 44 BEACH and MITCHELL In light of our thinking about these three troubling issues, and in light of our doubts about the generality of the Strategy Selection Model, we actively tried to make ourselves think outside the accepted canon and lore about decision making.  With the help of Kenneth Rediker, who was a graduate student at the time, we held weekly think-sessions in which we chased ideas.  Slowly, we began to see a structure to what we were thinking, and we began to write small essays trying to pin down our ideas.  These essays eventuated in our first attempt to go public (Mitchell, Rediker, and Beach, 1986).

After that first publication things got tough.  American journal reviewers seemed particularly reluctant to publish our work, even the empirical studies.  We did much better in Europe (e.g., Beach and Mitchell, 1987; Beach, et al., 1988; Beach and Strom, 1989).  To get the word out, we decided to put our ideas, and our research, in a book, but no American publisher was interested.  Finally, Britain's Wiley Ltd. took the risk, publishing Image Theory: Decision Making in Personal and Organizational Contexts in 1990.  Although we do not believe many people read the book, its mere existence seemed to give the theory legitimacy and interest quickly grew.

3.2 IMAGE THEORY BRIEFLY In the Image Theory view, the decision maker is an individual acting alone.  Of course, most decisions are made in concert with others, be it a spouse, a friend, business colleagues, or whoever.  But, even so, the decision maker has to make up his or her own mind and then differences of opinion must be resolved in some manner that depends upon the dynamic of the group.  That is, Image Theory does not regard groups or organizations as capable of making decisions per se, they are the contexts within which individual members' decisions become consolidated through convincing others, negotiation and politics to form a group product (Beach, 1990; Beach and Mitchell, 1990; Davis, 1992).  As a result, Image Theory focuses on the individual making up his or her own mind on the context³ of a social relationship or an organization, with the presumption that the result may later prevail, be changed, or be overruled when presented to others.

Each decision maker is seen as possessing values that define for him or her how things should be and how people ought to behave.  This involves such old-fashioned concepts as honor, morals, ethics, and ideals as well as standards of equality, justice, loyalty, stewardship, truth, beauty, and goodness, together with moral, civic, and religious precepts and responsibilities.  Collectively these are called principles and they are "self-evident truths" about what the decision maker (or the group to which he or she belongs) stands for.  They help determine the goals that are worthy of pursuit, and what are and what are not acceptable ways of pursuing those goals.  Often these principles cannot be readily articulated, but they are powerful influences on decisions.

³    The social or organizational context includes knowledge about others' views, information about the issue requiring a decision and the values and meanings (culture) shared by members of the relationship or organization (Beach, 1993).

Pg.# 46 and 47 BEACH and MITCHELL To state all of this a bit more formally: Decision makers use their store of knowledge to set standards that guide decisions about goals to pursue and strategies for pursuing them.  Potential goals and plans that are incompatible with (violate) the standards are quickly screened out and the best of the survivors is chosen.  Subsequent implementation of the choice is monitored for progress toward goal achievement; lack of acceptable progress results in replacement or revision of the plan or adoption of a new goal.

Each decision maker possesses a store of knowledge that is far greater than needed for the decision at hand.  That store can be conveniently partitioned into three categories, which are called images (Boulding, 1956; Miller, Galanter, and Pribram, 1960) because they are the decision maker's vision of what constitutes a desirable and proper state of events.  The categories are labeled the value image (principles), the trajectory image (the agenda of goals), and the strategic image (the plans that are being implemented to achieve the goals).

The constituents of the three images can be further partitioned into those that are relevant to the decision at hand and those that are not.  The relevant constituents define the decision's frame, which gives meaning to the context and provides the standards that constrain the decision.

There are two kinds of decisions, adoption decisions and progress decisions.  Adoption decisions are about adding new principles, goals, or plans to the respective images.  Progress decisions are about whether plan implementation is producing progress toward goal achievement.

There are two decision mechanisms, the compatibility test and the profitability test.  The compatibility test screens candidate principles, goals, or plans on the basis of their quality.  Actually, the focus is on lack of quality in that the candidate's compatibility decreases as a function of the weighted sum of the number of its violations of the relevant standards from the various images, where the weight reflects the importance of each violated standard.  If a single candidate survives screening by the compatibility test, it is adopted as a constituent of its respective image.  If there are multiple candidates and only one survives, it is adopted.  If there are multiple candidates and more than one survives, the tie is broken by application of the profitability test.  The profitability test focuses on quantity--choose the best candidate.  The Christensen-Szalanski formalization of the Strategy Selection Model has been incorporated into Image Theory to account for the many ways in which the candidates in the choice set can be evaluated and the best of them chosen.

PG. #51 BEACH and MITCHELL In short, we tailored our research emphases to colleagues in two different, but related, disciplines.  Decision researchers like equations and numbers, human resource researchers like interesting concepts.  By coaching our work in the appropriate terms we were able to arouse the interest of people in both disciplines.  Of course, it would be nice if the world would beat a path to your door after you invent a better theory, but it really does not happen that way.  There is a marketplace of ideas and marketing is as much a part of that marketplace as any other.  Our research strategy was designed to address this marketing problem, and it has worked well enough, in that other people have taken up the cause and extended the theory in ways we could never have imagined.  Moreover, this acceptance means we can now move on to examine a broader array of features of the theory.

The Road to Fairness and Beyond--ROBERT FOLGER

PG.# 56 FOLGER The turning point in events that led to my dissertation's themes, however, came indirectly.  At some point while perusing the social-comparison literature, I read the Adams (1965) chapter on inequity.  Here was something I could sink my teeth into!  Unlike ideas that seemed to go several directions at once, the Adams material had a focus that seemed promising.  Also, I saw significant "holes" in the research.  For one thing, Adam's own research stream had concentrated almost exclusively on the counterintuitive aspects of advantageous inequity ("overpay"), whereas I found the relative deprivation of disadvantageous inequity more interesting.  I also thought the lack of systematic investigations into the latter left a large number of questions unanswered.  Moreover, the Adams framework seemed well formulated in ways that would make useful operationalizations of the relevant constructs reasonably straightforward.  The more I read, the more convinced I became that predictions about reactions to underpayment were problematic because of these unanswered questions.  A series of early studies by Karl Weick (e.g., 1966) only confirmed this impression.

PG# 67, 68, & 69 FOLGER At the time, the mainstream journals reacted negatively to the presentation of results from those surveys in terms of procedural justice because the items referred not to choice or voice but to the demeanor and conduct of the police.  Having been influenced by Leventhal's (1980) approach to procedural variables, however, Tom conceived of procedures more inclusively.  Hindsight indicates we had addressed what Bob Bies later termed interactional justice (e.g., treating people with dignity and respect), but his writings on that topic had not yet appeared in print.

Bob became the next source for my recognizing the incompleteness of outcome-dominated thinking because of the frequency with which people care as much or more "how" things transpire as they do "what" they receive as tangible benefits.  The evolution of my thinking did not move in a linear fashion; various side-ways investigations also occurred (e.g., Folger and Konovksy, 1989; Folger, Konovsky, and Cropanzano, 1992).  I only realized gradually that traditionally conceived "outcomes" (e.g., pay amounts) often fail to have the psychic and symbolic impact of impersonal misconduct that demeans (e.g., publicly insulting subordinates in front of their peers).

Work by Bies influenced me in several ways.  His notion of interactional justice had a lasting impact not only on me but also on organizational science.  He also stressed social accounts, however, in ways that linger at least as much in my case.  Here, I saw that my RCT manipulations of "procedural" factors (e.g., Folger, Rosenfield, and Robinson, 1982; Folger and Martin, 1986) did not actually manipulate the structural aspects of procedures but instead applied social accounts to influence the participants' perceptions of procedures.  Bob's, having made that explicit, let to a follow-up study (Cropanzano and Folger, 1989) showing that the effects of both accounts and structural elements nonetheless paralleled one another.  Bies also reinforced my thinking that notions regarding legitimacy stretched beyond the structural design features of formal procedures per se--the very intuition that had guided me in using justification as the key non-outcome element in RCT rather than procedures or procedural justice.  In addition, I saw this beyond-structure impact as coming from social conduct, such as choices of how, when, and what to communicate (the accounts emphasis) but also including a range of interpersonal behaviors whether explicitly linked with communication efforts or not (such as giving someone the "cold shoulder," deliberately ignoring someone or taking pains to have nothing to do with them; e.g., Folger, 1993).

Having given an historical background on RCT, I turn now to Fairness Theory as an outgrowth from that line of thought.

4.3 FAIRNESS THEORY Fairness Theory or FT (e.g., Folger and Cropanzano, 1998, 2001; Folger, Cropanzano, and Goldman, forthcoming), herein reflects as yet unpublished developments in that model.  It stresses the theme of accountability impressions (not necessarily from conscious, deliberative thought--at least for some instances of initial reactions to events and persons) in relation to counterfactuals.  Accountability regarding blameworthiness can, in principle, reflect a continuum but in practice tends towards such poles as innocence versus guilt, blame versus credit, merit versus demerit.  FT posits that the motives and intentions presumed to underlie a person's mode of conduct can influence impressions about unfairness when the person seems at fault for wrongdoing.

The relevant counterfactuals--Would, Could, and Should--align roughly with elements from Schlenker's (e.g., 1997) triangle model of moral accountability as three interlocked components.  FT treats unfairness (holding someone accountable and blameworthy) as derived from a conjunction among these three facets relevant to impressions about human conduct.  Blame for unfairness amounts to a negative impression concerning each facet: What actually happened appears detrimental vis-à-vis three counterfactual representations (what did not happen) that each, in some sense, seem positive by comparison.

Pain contrasts negatively with pleasure as its (implicit) counterfactual, for example, just as guilt contrasts negatively with innocence.  Perceived unfairness metaphorically mirrors the "pain" associated with a perceiver's impressions about an incident (e.g., one person scathingly belittles another) that Would NOT have generated concern "if only" the incident had never taken place.  Blame also constitutes a negative (e.g., disapproving) impression related to at-least implicitly activated counterfactual representations concerning how the blamed person did not behave but Could and Should have behaved.

An example of an employee treating a customer in a rudely unfair manner (adapted from McColl-Kennedy and Sparks, 2003) illustrates these abstractions.  The rudely treated customer perceives unfairness with regard to the following conjunction of counterfactual standards or referents: "what could have occurred (being served with a smile), what should have occurred (being treated politely), and how it would have felt had an alternative action been taken (feeling happier)" (McColl-Kennedy and Sparks, 2003, 254).  Similarly, a third-party observer might consider the rudeness unfair and blame the employee for it if that perceiver's impressions include the sense that (a) the employee Could have smiled (e.g., did not have his or her mouth wired shut), (b) the employee Should have had more respect for the customer (e.g., by virtue of service-employees' duly assign responsibilities and obligations toward customers in general), and (c) the situation Would not have aroused any concern on the observer's part in the absence of the kind of incident that occurred.

PG.# 81 FOLGER Adams, J. S. (1965). Inequity on social exchange.  In I. Berkowitz (ed.), Advances in Experimental Social Psychology: 267-299.  New York: Academic Press.

Grand Theories and Mid-Range Theories: Cultural Effects on Theorizing and
the Attempt to Understand Active Approaches to Work
MICHAEL FRESE

PG.# 84 & 85 FRESE As is true of all human behavior, theory building is based on environmental forces and on person factors.  It has been my curse and my blessing to be overactive.  My overactive nature led me to believe that it was good to be active and to be in control of things.  Therefore, I quickly embraced theories that seemed to correspond with this prejudice.  The three theories that seemed to encompass what I stood for were Rotter's cognitive behaviorist theory (Rotter, Chance, and Phares, 1972), Seligman's learned helplessness theory (Seligman, 1975), and Hacker's action (regulation) theory (Hacker, 1973; Volpert, 1974).  Both Rotter's as well as Hacker's theories were indirectly related to a common source: Lewin's influence in Germany and in the U.S.  All my research centered around the themes of an active approach to work-life (the opposite of helplessness): Thus, I became interested in personal initiative as one such instance of an active approach.  Since an active approach means to explore, I also became interested in errors and how one can learn from errors.

PG.# 87 & 88 FRESE Our phenomenological orientation towards errors allowed us to make a discovery: When people are permitted and encouraged to make errors during training and are instructed to learn from errors, they perform better after training than when they are hindered from making errors.  This was surprising because most software trainers and a lot of theorists (e.g., Skinner and Bandura) had suggested otherwise: They favored the avoidance errors because they considered errors were too frustrating and inefficient for the learner, and that people would simply learn the wrong things.  Our so-called error training (later called error management training) proved to be superior to other methods of training people in computer skills (Heimbeck, et al., 2003; Ivancic and Hesketh, 2000; Keith and Frese, forthcoming).

Action theory argues that negative feedback is useful (Miller, Galanter, and Pribram, 1960): Action implies a goal (some set point that needs to be achieved).  Until one has achieved the goal, a person receives information that there is a discrepancy between the present situation and the set point (achievement of the goal, e.g., a person wants to travel to Rome and acknowledges that he or she is 500 miles away).  Thus, negative feedback presents information on what we have not yet achieved and it provides guidance to action.  Errors provide negative feedback but with a specific twist: An error implies that the actor should have known better.  It is the latter that produces the problems of blaming people--both oneself and others.

Therefore, we developed a training procedure (error management training) which gave participants explicit instructions to use errors as a learning device and not to blame themselves.  Participants are supposed to explore a system with minimal information provided; in contrast to exploratory training, error management training tasks are difficult right from the start, thereby exposing participants to many errors.  Error management training explicitly informs the participants of the positive function of errors; these so-called error management instructions are brief statements (we often called them heuristics because they allow us to deal with the error problem) designed to reduce potential frustrations in the face of errors: "Errors are a natural part of the learning processes!"  "I have made an error, great!  Because now I can learn!"  While participants work on the training tasks, the trainer provides no further assistance but reminds the participants of the error management instructions.  When comparing error management training with a training procedure that does not allow errors, error management training proved to be more effective across diverse groups of participants (university students as well as employees), training contents (e.g., computer training, driving simulator training), and training durations (1-hour training to 3-day training sessions), with medium to large effect sizes (Frese 1995).

PG. #103 FRESE What have I learned from my journey as a scientist who contributed both to a grand theory as well as to middle range theories?  The most important issue seems to me to have an open mind to the quirks and difficulties, as well as to beautiful coping strategies that people show in their environment--I think that curiosity and being able to wonder and be surprised are the hallmark of good science.  I am very interested in concrete phenomena and I suggest one should become intensively involved in real life phenomena (these may also be laboratory phenomena but I, personally, have been more interested in those that constitute important issues in society--not necessarily in my own society).  It helps to cultivate contacts across cultures and maintain contacts with various strata in society--varied experiences support the process of being surprised, stumbling across interesting phenomena, and of developing a wider net of theoretical ideas and methodological approaches.

Good research questions often start with wonderment and surprise.  We then have to work on understanding experiences and phenomena theoretically.  For this it is helpful to look at the world like a theory machine that attempts to understand all sorts of phenomena with theoretical concepts.  I remember that as students and young researchers my friends and I used to apply theories like a 2-year-old takes a hammer: We continuously attempted to use it to explain every phenomenon possible--in this way we quickly stumbled across the limits of the usefulness of these theories and, at the same time, we started to understand the theories better.

PG. # 104 & 105 FRESE In terms of methodology, I have come to rely more and more on a combination of qualitative and quantitative approaches.  I use structured interviews because differential anchor points are particularly problematic in any questionnaire research: What is high planning for one owner may be complete chaos for another one.  Structured interviews are useful, not only because they showed excellent validity in meta-analytic research (Hunter and Schmidt, 1996), but also because interviews gave me a chance to probe owners' answers and to understand precisely what they mean.  Questionnaires sometimes "lead" participants to certain answers.  For example, it would have been "leading" to ask directly for planning and activity within the questionnaire survey.  This is particularly true for cultural contexts in which it is improper to contradict others and where there is a tendency to create harmony (as in Africa).  All of this speaks for interviews.  At the same time, I want to have quantitative data to test hypotheses and to confirm and falsify them--therefore it is necessary to use coding procedures (I use very robust ones--not complicated content analyses).

I should warn you, however.  Not all of this writing immediately gets translated into academic success.  As a matter of fact, it is my observation that some of the empirical articles that I am most proud of (probably because they are dearest to my theoretical approach), have been the most difficult to publish.  My hunch is that they break with the typical approach to doing things and, therefore, invite criticism that reviewers are only too glad to provide.  On the other hand, those articles, that I am most proud of, are also often the ones that have the highest impact.  And that is after all what we are interested in.  We should never want to publish something just because we need another publication (well...at least never after we get tenure...).  I usually was driven to work hard on publications by the fact that I wanted to communicate something that I found to be important.  We should all want to shape and influence the development of science and knowledge rather than just be a smoothly functioning particle of a scientific machine.

Upper Echelons Theory: Origins, Twists and Turns, and Lessons Learned
DONALD C. HAMBRICK

PG.# 109 HAMBRICK The central idea of upper echelons theory is that executives act on the basis of their highly personalized interpretations of the situations and options they face.  That is, executives inject a great deal of themselves--their experiences, personalities, and values--into their behaviors.  To the extent those behaviors are of consequence, say in shaping strategy or influencing the actions of others, organizations then become reflections of their top managers.

PG.# 120 & 121 HAMBRICK While doing field research in the early 1990s, interviewing CEOs about their top management teams (TMTs), an unsettling fact become clear: Many, many top management teams have few "team" properties.  They consist primarily of solo operators who are largely allowed to run their own shows, who interact minimally, sometimes rarely seeing each other.  Such a condition poses a problem for upper echelons theory, or at least for that aspect that deals with how TMT characteristics affect firm outcomes.  For, if TMTs are highly fragmented, then team characteristics will matter very little to firm outcomes.  Instead, firm outcomes are the outgrowth of a host of narrow, specialized choices made by various individual executives (Hambrick, 1994).

These observations lead me to develop and elaborate on the concept of "behavioral integration" within TMTs.  Behavioral integration is the degree to which mutual and collective interaction exists within a group, and it has three main elements or manifestations: information exchange, collaborative behavior, and joint decision making.  That is, a behaviorally integrated TMT shares information, shares resources, and shares decisions.  In its focus on substantive interaction, behavioral integration is related to, but distinct from, "social integration," a concept that places more emphasis on members' sense of group pride or team spirit (Shaw, 1981).

In my initial presentation of behavioral integration, I proposed an array of factors that will determine the degree of behavioral integration that will exist in a given TMT.  These factors included environmental factors, organizational factors, and the CEO's own personality or performance.  Recently, Simsek, et al. (forthcoming) collected data on TMTs in 402 small- and mid-sized companies, verifying some of the key predictors of TMT behavioral integration.  In particular, they found that behavioral integration was positively related to the CEO's own collectivist orientation and tenure, and negatively related to TMT size and several types of TMT diversity.

PG.# 122 & 123 HAMBRICK Even though upper echelons theory has made its mark on the organizational sciences, I have some lingering disappointments about our shortcomings in testing and verifying the theory.  Foremost, I am disappointed that we have not done a better job of directly examining the psychological and social processes that stand between executive characteristics on the one hand and executive behavior on the other.  Namely, we have done a poor job of getting inside "the black box" (Lawrence, 1997; Markoczy, 1997).  For example, when we observe that long-tenured executives engage in strategic persistence, why is that?  Are they committed to the status quo?  Risk-averse?  Tired?  or What?  Even examination of executive psychological properties is not exempt from such questions.  So, for example, when we find that executives who have a high tolerance for ambiguity perform well when they pursue growth-oriented strategies (as opposed to harvest-oriented strategies) (Gupta and Govindarajan, 1984), why is that?  What's going on?  How does tolerance for ambiguity affect executive behaviors?  Even though we have talked for a long time about the need to get inside the black box (to the point that it has become a cliché to express the need), we still have made exceedingly little progress in doing so.

In this same vein, we have little evidence that executives filter the information they confront in any way that resembles the three-stage process depicted here as Figure 6.1.  For example, do executives with technology backgrounds scan more technology-oriented information sources than those who don't have technology backgrounds?  Do they notice, or perceive, more of the technology information they scan?  Do they require fewer pieces of information to form an opinion about a technology trend?  In short, there is a pressing need to gather data on the actual information-processing behaviors of individuals (and teams) in strategic decision-making situations.  Pursuing this perspective will certainly require laboratory-type or experimental research designs, as well as the tools and concepts of the psychologist.

A related disappointment is that we have done an inadequate job of disentangling causality in upper echelons studies.  Do executives make strategic choices that follow from their own experiences, personalities, and biases, as posited by the theory?  Or do certain organizational characteristics lead to certain kinds of executive profiles?  Over time, a reinforcing spiral probably occurs: managers select strategies that follow from their beliefs and preferences; successors are then selected according to how well their qualities suit that strategy; and so on.  Thus far, relatively few upper echelons studies have been designed in ways as to allow convincing conclusions about casual direction.

Goal Setting Theory: Theory Building by Induction
EDWIN A. LOCKE and GARY P. LATHAM

PG.# 128 LOCKE and LATHAM Life is a process of goal-directed action.  This applies both to the vegetative level (e.g., one's internal organs) and to the level of purposeful choice (Locke and Latham, 1990).  The conscious mind is the active part of one's psychology; one has the power to volitionally focus one's mind at the conceptual level (Binswanger, 1991; Peikoff, 1991).  Volition gives one the power to consciously regulate one's thinking and thereby one's actions.  Goal setting theory (Locke and Latham, 1990, 2002) rests on the premise that goal-directedness is an essential attribute of human action and that conscious self-regulation of action, though volitional, is the norm.

We do not deny the existence of the subconscious nor its power to affect action.  In fact, the subconscious is essential to survival in that only about seven separate elements can be held in focus awareness at the same time.  The subconscious operates automatically and serves to store knowledge and skills which are needed in everyday action.  The subconscious is routinely activated by our conscious purposes and also determines our emotional responses (Locke, 1976).

PG.# 137 & 138 LOCKE and LATHAM We recognized early on, again by introspection, that goal commitment is critical to goal effectiveness.  We, like everyone else, knew that most New Year's resolutions are abandoned.  Lofty sounding intentions do not necessarily indicate commitment to specific goals.

The question was: How do you get goal commitment?  Our initial belief was: through participation.  Participation in decision making (pdm) was a popular topic of study following World War II.  Locke (1968) predicted that participation would enhance goal commitment.  We did not pursue this matter for some time; then, starting in the 1970s, there was chaos in the literature on this topic.  The reason was largely political (Wagner and Gooding, 1987).  For many scholars participation was viewed not only as a potentially useful managerial technique, but as a "moral imperative."  Because it was considered a "democratic" practice and an antidote to fascism, the results simply had to be supportive of the former ideology.

Locke and Schweiger (1979) conducted a literature review.  They discovered that the interpretation of many pdm studies had been distorted to make the results appear supportive.  When the data were interpreted objectively, pdm only had a minimal effect on performance.  Strongly worded arguments on this issue went back and forth in the literature for years; heated debates took place at professional meetings.

Latham and I, however, stuck to our core principle: "reality (facts) first."  We had no "moral" bias either for or against pdm.  As noted, we both initially expected pdm to lead to higher goal commitment, because the positive effects of pdm had been touted so much in the earlier literature.

The thrill of inductive, programmatic research is akin to that of being a detective.  Latham's doctoral dissertation involving logging crews revealed that productivity was highest in those who were randomly assigned to the participatively set goal condition and less educated (Latham and Yukl, 1975).  This supported the value of pdm--but there was a confound.  It turned outh that goal difficulty was also significantly higher in that condition.  The same result was obtained in a field experiment (Latham, Mitchell and Dossett, 1978).  Then a series of laboratory experiments showed that when goal difficulty was held constant, participation in goal setting had no effect on goal commitment or performance. (Latham and Marshall, 1982; Latham and Saari, 1979a; Latham and Steele, 1983).  All this seemed to indicate that the initial pdm effects had simply been goal effects.  The issue of pdm was momentarily settled.

Soon, however, a series of studies by Miriam Erez and her colleagues appeared (e.g., Earley and Kanfer, 1985; Erez, Earley and Hulin, 1985).  The results of this work can be summarized in a single sentence: Latham is wrong; participatively set goals work better than assigned goals.  Instead of attacking Erez, Latham posed the question: why the differences?

When competent researchers obtain contradictory findings, the explanation may lie in differences in methodology.  We decided to resolve the conflict in a revolutionary way.  Latham and Erez would design experiments with Locke, who was a close and respected friend of both parties, agreeing to serve as a helper and a mediator between us.  The result was a series of experiments jointly designed by the three of us.

PG.# 139 LOCKE and LATHAM Atkinson (1958), a student of McClelland, predicted that one's motivation is highest when task (goals were not part of his model) difficulty is.50.  This suggested a possible curvilinear (inverted-U) relationship between goal difficulty and performance.

In contrast, expectancy theory (Vroom, 1964) states that the force to act is a multiplicative function of valence, instrumentality, and effort-performance expectancy.  Holding the first two factors constant, the theory predicts a positive, linear association between expectancy and performance.  However, difficult goals are harder to attain than easy goals, thus we had found a negative linear relationship between expectancy of success (high expectancy meant easy goals) and performance (Locke, 1968).

All three theories could not be correct.  Aided by an insight by Howard Garland, Locke, Motowidlo, and Bobko (1986) resolved the puzzle.  When goal level is held constant, that is, within any given goal group, the positive linear relationship asserted by expectancy theory is correct.  Between groups, when goal level is varied, the relationship is negative.  This does not contradict expectancy theory, because expectancy theory assumes that the referent is fixed.  When Bandura's self-efficacy measure is used (which averages a person's confidence estimates across multiple performance outcome levels) both the within and between group associations are positive.  The curvilinear relationship between expectancy, or goal difficulty, and performance as suggested by Atkinson replicates only when there are a substantial number of people in the hard goal condition who reject their goals (Erez and Zidon, 1984; Locke and Latham, 1990).

PG.# 143 & 144 LOCKE and LATHAM Our approach to theory building effort is inductive.  Induction means going from the particular to the general.  This is in contrast to the "hypothetico-deductive" method.  The latter view stems from a long line of philosophical skeptics, from Hume to Kant to Popper to Kuhn.  The core premise of this view is that knowledge of reality is impossible.  Popper, believed that because theories are not based on observations of reality, they can start, arbitrarily, from anywhere.  Thus, theories cannot be proven, they can only be falsified by testing deductions from them.  Even falsification, Popper asserted, never gets at truth.  Induction is rejected.  If Popper were correct, scientific discovery would be impossible.  But history refutes this view.

The history of science is the history of discoveries made by observations of reality, and integrated into laws and principles.  Subsequent discoveries do not necessarily invalidate previous ones, unless errors of observation or context-dropping were made.  They simply add to knowledge.  Mankind did not get from the swamps to the stars by eschewing the search for knowledge and seeking only to disprove arbitrary hypotheses.

Galileo, for example, did numerous experiments with freely falling objects, objects rolling down inclined planes, swinging pendulums, and trajectories of objects and induced the law of inertia, the constancy of gravity, and the laws governing horizontal and vertical motion.  He also invented an improved telescope and discovered four moons of Jupiter.  He proved that Venus orbits the sun--giving further credence to Copernicus's heliocentric theory.  Newton discovered that white light is composed of different colors by doing experiments with prisms.  He drew upon the observations of Kepler and Galileo to discover the laws of motion.  Especially revolutionary was the idea that all bodies are attracted to one another by a force (gravity) whose magnitude is proportional to the masses of the bodies, and inversely proportional to the square of the distance separating them.  With this knowledge, including his invention of calculus, he was able to explain the actions not only of the planets but of the tides.  Both Galileo and Newton used observation to gather data, conduct experiments, and then integrated their observations into a theory.

Einstein agreed: "Turning to the subject of the theory of [special] relativity, I want to emphasize that this theory has no speculative origin, it rather owes its discovery only to the desire to adapt theoretical physics to observable facts as closely as possible" (Einstein, 2002: 238).

Contrast Galileo, Newton, and Einstein to Descartes who argued that one can deduce the components of matter, the nature of the planets, moons, and comets, the cause of movement, the formation of the solar system, the nature of light and of sunspots, the formation of the stars, the explanation of tides and earthquakes, the formation of mountains, magnetism, the nature of static electricity and chemical interactions--all from what he claimed were innate ideas discovered intuitively.  Not surprisingly, every single one of his theories was wrong.²

Of course, theory building does include deduction.  But, the major premises that form the beginning of any syllogism (e.g., "all men are mortal") have to be established by induction, or else the conclusion, even if valid in "form," will be false.

What then does induction involve?

²    The comments about Galileo, Newton, and Descartes were based on portions of a forthcoming book by David Harriman.  These portions were published in The Intellectual Activist, vol. 14, nos. 3-5 (2000) and vol. 16, no. 11 (2002).  The authors are indebted also to Stephen Speicher for providing the information on Einstein.

Do Employee Attitudes towards Organizations Matter?
The Study of Employee Commitment to Organizations
LYMAN W. PORTER, RICHARD M. STEERS and RICHARD T. MOWDAY

PG. #171 & 172 PORTER, STEERS and MOWDAY The late 1960s and early 1970s in the United States were both turbulent and tranquil.  Campus unrest over the war in Vietnam and civil rights wreaked havoc across many college campuses as students, and sometimes faculty, picketed, struck, and otherwise protested situations that they thought were both unjust and unfair.  Occasionally, the demonstrations turned violent and at its peak collective action was sufficiently strong and vocal to bring down a sitting U.S. president.  At the same time, however, most major U.S. companies remained bastions of relative tranquility as blue- and white-collar employees went to work every day and worked hard for a better life.  The "organization man" described in William H. Whyte's classic 1952 book of the same name was alive and well.  Managers (almost exclusively male) wore business suits and downsizing was not yet on the corporate radar screen.  People typically worked for one company throughout their career and retired at age 65.  While college campuses may have been in crisis, everything was "normal" in Corporate America.

These two contrasting pictures, one of strife and turmoil and one of stability and tranquility, puzzled many social observers of the time.  Exactly what was going on here?  Why were some employees, be they university professors or corporate managers, highly committed to their organizations, while others were indifferent or even antagonistic?  What caused some employees to form emotional bonds and strategic attachments to their organizations, while others quit as soon as they had a chance?  And throughout it all, how could organizations entice their best employees to remain with them for the duration?  These issues intrigued social scientists of the time because they forced organizations--and to some extent societies--to grapple with fundamental questions about the legitimate role of employees in work organizations.  Scholars began asking questions about the nature of employee commitment to organizations, as well as how commitment developed or failed to develop over time.  How did employers and employees define their mutual dependencies and how did they negotiate and implement psychological contracts?  From a research standpoint, the search was on for what became known as the causes and consequences of organizational commitment.

PG.# 185 & 186 PORTER, STEERS and MOWDAY The weight of the evidence suggests that employee attitudes toward the organization are behaviorally relevant.  However, the magnitude of these relationships reported in the literature suggests that organizational commitment, while important, is obviously not the only attitude that influences behaviors in the workplace.  Rather, the determinants of employee behavior in the workplace are complex and involve attitudes toward multiple features of work (e.g., the job and the organization), behavioral intentions, and contextual factors that facilitate or inhibit employees from acting on their intentions.  Given that this line of research on organizational commitment was motivated to redress the imbalance in research on job satisfaction and other job-focused attitudes that existed at the time, it seems reasonable to conclude that subsequent research has demonstrated that a broader array of attitudes are important to understanding behavior at work.

Even so, the world of work has changed dramatically since our initial research on organizational commitment in the 1970s and 1980s.  Downsizing and minimum wage jobs have become a strategy of choice for many firms in order to meet intense competitive pressures, while employees who retain their jobs are under increasing pressure for increased productivity and efficiency.  Working hours, including both voluntary and involuntary overtime, as well as stress levels, are on the increase.  Increased globalization pressures have led to a marked expansion of overseas manufacturing and outsourcing, even among white-collar and professional employees.  Meanwhile, younger employees of both genders are becoming increasingly vocal about securing a suitable work-family balance just at the time when such a balance may be the more difficult to achieve.  Above all, gone are the days when most young high school and college graduates sought a career and a company for the long term.

In this regard, Peter Capelli (1999: ix) has noted that "[T]he older, internalized employment practices, with their long-term commitments and assumptions, buffered the employment relationship from market pressures, but they are giving way to a negotiated relationship where the power shifts back and forth from employer to employee based on conditions in the labor market."  Even so, Capelli acknowledges that most contemporary firms still require some form of employee commitment to meet their goals.  To accomplish this, he observes that many companies have tried to refocus employee commitment away from the company as a whole and towards specific aspects of the company, such as work teams.  "For many jobs, commitment to the corporation as a whole is largely irrelevant as long as the employees feel commitment to their team or project" (p. 11).  At the same time, he points out that in recent years "voluntary turnover has been less of a problem for the corporate world because virtually all corporations have been downsizing at the same time, creating a big surplus of talent on the market and also restricting those who quit voluntarily" (p. 6).

Developing Psychological Contract Theory
DENISE M. ROUSSEAU

PG.# 191 ROUSSEAU Valery (1938, 1958) said, "There is no theory that is not a fragment, carefully prepared of some autobiography."  In my case, family background is as powerful as my academic training in laying the ground work for investigating the dynamics of employment relations.  My father hated his job.  He probably should have been a high school history teacher or basketball coach.  Instead of going to college or pursuing work that interested him, with a large number of brothers and sisters to support, and after serving in the U.S. Navy during World War II, he went to work for the telephone company first as a lineman and then a cable splicer, ultimately working there for thirty-six years.  Though the work was physically somewhat hard, it was the political and abusive behavior from telephone company foremen and managers that my father talked about at dinner.  (Later as an adult, I did some genealogical research and found out that during the late 1880s my French-Canadian great-grandfather had been a telephone company supervisor.  Dad was aghast).  My father's dissatisfaction with his job and career led me to focus on the work lives of workers, and especially of employees, those who work for somebody aside from themselves.  In hindsight, it seems natural that I became an industrial psychologist.

PG. #193 & 194 ROUSSEAU Psychological contract comprises the beliefs an individual holds regarding an exchange agreement to which he or she is party, typically between and individual and an employer (Rousseau, 1995).  These beliefs are largely bases upon promises implied or explicit, which over time take the form of a relatively stable mental model or schema.  A major feature of a psychological contract is the individual's belief that an agreement exists that is mutual; in effect, his or her beliefs in the existence of a common understanding with another that binds each party to a particular course of action.  Since individuals rely upon their understanding of this agreement in the subsequent choices and efforts they take, they anticipate benefits from fulfilled commitments and incur losses if another fails to live up to theirs, whatever the individual interprets another's commitments to be.

Psychological contract theory is construct-driven.  The features of this construct, particularly its schematic nature, give rise to its dynamic properties.  These dynamics are central to its distinctive consequences, antecedents, and boundary conditions.  A central dimension of this construct is incompleteness, in that the full array of obligations associated with the exchange are typically not known or knowable at an exchange relationship's outset; requiring the contract to be fleshed out over time.  Incomplete contracts are completed, updated, and revised through processes that affect both the degree of actual agreement between the exchange parties as well as the psychological contract's flexibility in the face of change (cf. Rousseau, 2001).  As a form of schema or mental model, psychological contracts become more durable as they move toward a high level of completeness, wherein they enable prediction of future actions by contract parties and effectively guide individual action..  This durability also poses difficulty in response to changing circumstances.  Sources of information used in developing and completing the psychological contract include the agents of the firm (e.g., managers and human resource representatives) as well as the social influence of peers and mentors, along with administrative signals (e.g., human resource practices) and structural cures (e.g., informal network position) to which individuals are exposed (Rousseau, 1995; Dabos and Rousseau, 2004b).

PG. #209 & 210 ROUSSEAU I worry a bit about generalizing too much from my own experience.  This account plays up my personal and professional circumstances and the fact that I have focused a long time on the same research domain.  Not every interesting problem is anchored in a scholar's life history.  The problem can be created by need, opportunity, or circumstance.  I also doubt that a good theory requires a single dominant theme in one's research over time.  Monad and Jacob managed to discover how gene functioning could be switched on and off and win a Nobel Prize, without having any apparent personal angle to the problem, and each went on to study a variety of other things.  The best advice implicit in my experience is to experiment with ways of working that help you learn and seek out others to help and learn with you.  Here are some ways of working that I found useful.

Figuring out the right question to ask has to be the hardest part.  A good question can guide discovery because even if the answer proves it wrong, you move forward (Wilson, 1999).  The question "Do people think in psychological contract-like ways?" arose from talking with Max Bazerman.  Formulating that question was important since it had the possibility of disconfirmation, and the potential to establish convergent and discriminant validity.  Good questions also call attention to mediating processes that underlie casual relationships.  It is not enough to know that something is related to something else.  Why and how are what matter.

Talking to smart people who think differently than we do helps in identifying important questions.  I was fairly systematic in meeting with colleagues at Northwestern, in the Business School, Psychology, Communications, and Law to see what suggestions they might have for exploring the notion of a psychological contract.  Being at a good research university with a diverse faculty is a great asset.  I used these conversations to get pointer knowledge about what to read and whom else to talk with.  I learned from their answers to the query, "What do you think would be a good question to ask about X (psychological contract, employment relationships, agreements between workers and employers, etc.)?  Trying to explain what I thought a psychological contract was and why it mattered invited informed and useful criticism, even if some of my colleagues might refer to it as the "so-called 'psychological contract'."  Talking with others made it easier to place the construct of a psychological contract into a theoretical framework.  The construct became clearer and more concrete to me while becoming more nuanced and differentiated from look-alike notions of expectations with which the field was already very familiar.  I also learned a lot from taking the theory on the road and doing colloquia.  (NB: This may work better if you aren't looking for a job.)

The Escalation of Commitment: Steps toward an Organizational Theory
BARRY M. STAW

PG. #233 - 235 STAW In advising young scholars interested in developing new theory, I would offer the following tips from escalation research:

First, I would consider the events of the world (from business, government, and politics) to be as rich a source of ideas as any academic literature.  One's own personal and family experiences can also be mined for interesting research ideas.  In the case of escalation, I was not only prompted to the research idea by observing the U.S. involvement in Vietnam, these observations took on particular meaning given my prior experiences with the military draft.  In addition, when I derived my specific hypotheses on self-justification, I drew on some vivid personal recollections.  Once, on vacation from college, my father asked me to look over some financial statements to see whether he should buy a particular retail store.  When I studied the numbers (with my recently acquired knowledge of introductory accounting) and pronounced the purchase to be a waste of money, my father drew a line through both the revenue and cost figures.  He said that the financial forecasts were far too conservative.  When I protested, he admitted that it really didn't matter since he had already purchased the store a few weeks earlier!  Experiences such as these can be an invaluable tool for constructing theory, since they have more depth and meaning than any perusal of the research literature.

Although I tout experience over literature reviews, I still think it is important to confront a potential research question with as broad a theoretical arsenal as possible.  Certainly my initial studies of escalation were shaped in large part by my earlier dissertation.  I also believe that the theory's transformation from a psychological to a more interdisciplinary model may have been aided by prior academic training.  At the time of my graduate work at Northwestern University, the doctoral program in organization research was almost entirely sociological.  Though I was greatly influenced by social psychologists such as Thomas D. Cook and Donald T. Campbell, most of my colleagues and faculty advisors were interested in macro or sociological questions.  Therefore, it was probably easier for me than other psychologists interested in escalation to make the transition from a largely individually-oriented theory to one that is also based on social and organizational forces.

A third piece of advice from work on escalation would be to approach research questions with as much methodological flexibility as possible.  As I have noted, my research started with a series of laboratory experiments designed to show that, under certain conditions, people may throw good money after bad.  Unfortunately, my own theoretical reasoning did not really broaden until I had worked on some case studies of escalation.  Only then did I realize that escalation was an interdisciplinary problem with multilevel forces at work.  As a result of this experience, I am now a firm believer in the power of grounded research, at least as a means of theory formulation.  Such investigations need not come in the form of publishable case studies.  They can also result from in-depth examinations of organizational events or from interviews with key actors in a social situation.  Regardless, grounded observations will likely enrich your hypotheses and broaden your understanding of an organizational phenomenon.

A fourth tip might concern the orchestration or sequencing of research studies.  When I entered academia, I had the naive impression that discoveries would be followed by press conferences and then a flurry of follow-up research.  Forget the press conferences and be satisfied with a few colleagues (and relatives) reading a paper.  Also forget the flurry of follow-up studies, if you are not willing to do them yourself.  Rarely does a single study ignite enough interest to start a genuine stream of research.  So be prepared to carry on alone for a while.  And, even when others have been brought into a line of research, do not expect them to pursue the issue in exactly the way you might prefer.  That is why I initiated case studies and archival research on escalation.  Without some intervention, I feared that escalation research might stagnate and eventually die in the laboratory.

My fifth and final tip relates to the process of theory formulation itself.  The field or organizational behavior is fond of summary models using a series of boxes and arrows.  I too have found them to be helpful devices in illustrating a theoretical process or set of mechanisms.  My complaint is that much of our field equates the graphical listing of variables with theoretical formulation.  Therefore, we need to be constantly reminded that the goal of theory is to answer the question of "why" (Kaplan, 1964; Merton, 1967).  Strong theory delves into the connections underlying a phenomenon.  It is a story about why acts and events occur, with a set of convincing and logically interconnected arguments (Sutton and Staw, 1995).  Hence, my advice for young scholars is to use diagrams as an aid to theoretical reasoning, but not as an end in itself.  With luck, your models will have implications that cannot be seen with the naked (or theoretically unassisted) eye, and may have implications that run counter to common sense.  If successful, the product may even satisfy Weick's (1989) dictum that good theory will explain, predict, and delight.

On the Origins of Expectancy Theory
VICTOR H. VROOM

PG. #251 & 252 VROOM Let me digress from a presentation of the formal derivations from the theory to a more personal topic.  Does the theory help me to describe or make sense of my own behavior surrounding its development?  How do I now make sense of my own choices using the expectancy theory framework?

It is now very clear that I was very highly motivated to complete Work and Motivation.  On many nights, I was still working in the university library when it closed at midnight, and I was asked to leave.  Developing a theory which made sense out of otherwise disparate findings was something that was "Hebb like," albeit in a totally different domain.  Furthermore, it represented a tangible effort at integrating the two disciplines of psychology, which Cronbach had advocated.  Finally, it united theory and application in a manner which might have received Kurt Lewin's blessing.  For these and probably many other reasons, writing Work and Motivation was something that I had to do.  At times, it felt like a labor of love and, at other times, a neurotic compulsion.  It was completely positively valent endeavor.

It was also clear that this strong desire was intrinsic and not based on a well-conceived career strategy.  My colleagues at Penn kept telling me that what I was doing was the province of those with tenure and that empirically based articles were a far safer course for those on a three-year contract.  If they were correct, I was jeopardizing my chances of getting promoted, at least at Penn by doing what I was doing.

Complementing this positive valence was a reasonable expectancy that I was capable of "pulling it off."  I have previously alluded to the many sources of support and encouragement I had received during my early academic years.  These served to sustain my belief that I was capable of the task at hand and made it possible to ignore the voices pointing to the peril that could lie ahead.  I also received support from my doctoral students at Penn who read the chapters as they were produced and made many helpful suggestions.  Prior to leaving Penn, I had met Gordon Ierardi, then editor of a highly prestigious Wiley psychology series.  Gordon asked to review my almost completed manuscript on Work and Motivation and subsequently extended a contract.

PG. #256 VROOM At least once a week, I receive an e-mail from a student somewhere around the globe asking for my current thoughts on expectancy theory.  The specific requests vary.  The student has been asked to write a paper or make a presentation on a theorist and has chosen me.  Would I explain the theory to them in simple terms or tell them how I came up with the theory or reveal some anecdote about my personal life that would add "punch" to their presentation?  I am typically in a quandary about how to respond.  Seldom do I have the time to do justice to the request.  Now that this chapter will be available, I have something to which to refer them that might answer their questions.

Buy my quandary is more than that.  The truth is that I have difficulty jumping "back into the skin" of a 25 year old on a mission.  Even writing this chapter was not easy.  Fortunately, I had the aid of notes of previous reminiscences to make the task easier.  Expectancy theory was a chapter in my life, not my whole life.  Subsequent events have produced marked changes in my personal agenda.  Some say that I am still "driven" but with different priorities.  In the 1950s and early 1960s, I wore psychology "on my sleeve."  It was the only path to my personal truth.  Business schools and schools of management were, in my mind, lower-class institutions uninitiated in the scientific method.

Perhaps, it was the nine years at Carnegie Mellon or subsequently the thirty plus at Yale helping to found and then teach in their new School of Management that has produced a different frame of mind.  Or, perhaps, it is simply the passage of time that has dimmed the single-minded idealism of youth and replaced it with a more balanced and societal anchored quest.  Forty years of attempting to make the behavioral sciences relevant to present and future managers has made me highly sympathetic to their needs.  Furthermore the science of psychology is no longer my primary goal but is rather a means to the goal of helping managers to better understand themselves, those with whom they work, and the organizations they serve.  I like to think that I have not abandoned the scientific method.  Instead, I have tried to use it in ways to help managers deal with the complexities in their world (Vroom and Yetton, 1973; Vroom and Jago, 1988; Vroom, 2003).

Along with this changed role of science in my life has come an increased impatience with the trappings of formal science.  Often the postulates, assumptions, derivations, and formal mathematical models of my youth seem like a premature attempt to mimic the physical sciences and do little to advance the state of our knowledge, particularly knowledge that is actionable.  Furthermore, I no longer seek one lens or theory that will explain or unify it all.  Pluralism and the interplay of conflicting modes of sense-making have replaced my need for order and convention.  Perhaps the jazz musician and the psychologist have finally come together!

Double-Loop Learning in Organizations: A Theory of Action Perspective
CHRIS ARGYRIS

PG. #261 & 262 ARGYRIS I began my work on organizational behavior by observing several puzzles.  The first was that human beings created policies and practices that inhibited the effectiveness of their organizations.  Why did human beings create and maintain these policies and practices that they judged to be counterproductive?

The second puzzle, human beings reported a sense of helplessness about changing these policies and activities because they were the victims of organizational pressures not to change them?  How did human beings create organizational pressures that inhibited them from changing the phenomena they saw as counter-productive?  Is it possible to help individuals and organizations to free themselves from this apparent self imposed enslavement?  I begin my inquiry with an examination of how action is produced be it productive or counterproductive.  I then examine the role of learning focusing on learning that challenges the existing routines and the status quo.  Next, I present a model of a theory of action that explains the puzzles described above.  This is followed by a description of a theory of action that can be used to resolve these puzzles.  Next, is a description of intervention processes that are derivable from the theory that can be used to get from here to there.  This is followed with discussions of some implications for scholars in developing theory and conducting empirical research that leads to actionable knowledge.  I close with some personal observations of my tribulations over the years while building the theory and conducting research.

PG. #273 - 274 ARGYRIS It is important that scholars take more initiatives in building theories and in conducting empirical research that questions the status quo.  The first reason is that it makes it less likely that scholars will become, unintentionally, servants of the status quo.  The second reason is that identifying possible inconsistencies and inner contradictions is a powerful way to examine our own inconsistencies and inner contradictions.  For example, we espouse that we should describe the universe (that we construct) as accurately and completely as possible.  This means that we should include research on how the universe would act if it was being threatened.  In order to conduct such research we require empirical research on how the existing status quo inhibits learning and produces inner contradictions.  This, in turn, requires the development of testable theories about new and rare universes, which, if implemented, would threaten the status quo.

The long-term commitment to describing the universe as it is inhibits the study of new universes that would encourage liberating alternatives and double-loop learning.  For example, the core concepts of the behavioral theory of firms include the existence of competing coalition rivalries and limited learning.  The limited learning is partially caused by the limited information processing capacity of the human mind.  This claim is, in my opinion, valid.  Another claim that may also be valid is that the competing coalitions (and other organizational defensive routines) may also limit learning.  To my knowledge, scholars have not tested this claim.  More importantly, they appear not to do so because they (e.g., March) express doubts that such factors as mistrust produced by competitiveness can be reduced (see Argyris, 1996).  Burgelman also doubts that organizational defensive routines can be reduced.  He also acknowledges that not testing this claim could have anti-learning and self-sealing consequences (see Argyris, 2004).

Similar questions may be raised about the rules and norms of conducting rigorous empirical research.  For example, the theory-in-use (not espoused theory) of rigorous research is consistent with Model I.  It is the researchers who are in unilateral control.  The result is that the empirical propositions when implemented create a world consistent with Model I (Argyris, 1980, 1993).  For example, studies on communication to generate trust advise that, when communicating to "smart" people, offer them several views.  When communicating to "those judged to be less smart," offer one view.  Implementing this advice requires that the implementer cover up the reasoning behind it.  It also requires that the implementer covers up the cover-up.  None of these consequences are explored by the researchers.  Yet, all of them are consistent with Model I theory-in-use; a theory-in-use that facilitates mistrust.

Studies on frustration and regression conclude that mild frustration actually produces creative reactions.  After a certain frustration threshold is passed, the predicted regression results (Argyris, 1980, 1993).  Let us assume that a leader wishes to generate the creativity predicted during the early stages.  This would mean that she would have to create low to moderate frustration.  It also is likely that she cannot tell the "subjects" of her intention because doing so could lead the subordinates to react negatively to what they may interpret as her manipulation.  If some do not react negatively then she would have created sub-groups that conflict with each other.  In short, the leader would have to cover up that she is covering up.  If there are members of the group who believe that she is covering up, they too may cover up their attributions.  They would place these thoughts and feelings in their left-hand column.  The multilevel cover-up will make it more difficult to assess the arrival of the threshold point beyond which regressions would appear.

All of these issues arise when attempts are made to implement the knowledge produced in the original experiments.  These conclusions appear to hold for humanities research intended to bypass the Model I theory-in-use.  Indeed the same appears to be true for interpretive research where testing stories is a primary methodology (Argyris, 2004).

These and other similar observations (Argyris, 1997) raise doubts that our theories and our research methods are neutral to normative features of everyday life.  The theories and empirical research methodologies are highly influenced by Model I and organizational defensive routines.  They are not neutral whenever social scientists create theories limited to Model I and use research method whose theory-in-use is Model I.  Moreover they get rewarded for doing so by the norms of their scholarly community, they become skillfully unaware of the limits of their claims, especially about neutrality and the promise of a scientific enterprise that does not limit truth-seeking (Miner and Meziac, 1996).

13.4 THE ROLE OF INTERVENTION Intervention is the most effective methodology for empirical research, related to double-loop learning.  Interventions are social experiments where understanding and explanation are in the service of valid implementation intended to be of help.  It is difficult for an interventionist to obtain permission and request cooperation from "subjects" on the claim that the research may be helpful and then stop before providing such help.  The "subjects" would feel betrayed because the promise to be of help includes implementation (Argyris, 2003).  These feelings of betrayal are being built up within society--including congressmen and foundations--by researchers who have promised that they are committed to producing valid and actionable knowledge but who fail to fulfill their promises (Argyris, 1993; Argyris and Schon, 1996; Johnson, 1993).

Interventions require skills for producing internal and external validity.  Such skills can be developed and taught.  Interventionists also need to develop Model II skills if they choose to give implementable validity equal status.  Implementable validity has its own internal and external features.  Internal implementable validity is established by the degree to which the claims in the proposition actually lead to the specified consequences.  For example, it is claimed that Model I theory-in-use is an important cause of organizational defensive routines.  This casual claim can be tested through observations.  External implementable validity is assessed by the extent to which specified organizational defensive routines are reduced when human beings become skilled at Model II theories-in-use.  The former prediction is internal as long as it is not implemented.  The moment we implement the claim the validity of the implementation is external.

Where does Inequality Come from? The Personal and Intellectual Roots of Resource-Based Theory
JAY B. BARNEY

PG.# 282 BARNEY
In retrospect, this outcome should not have surprised me.  The mythology of equality was so entrenched among those that administered this educational program that they actually lacked the ability to recognize differences among the students.  Giving everyone the same grade was simply their way of making sure "no one got left behind."  Of course, in this Lake Wobegone world where all students are above average, there is also no room for excellence, no room for uniqueness, and no room for distinction.  And, as it turned out, no room for me.  I left he program after one semester.

Thus, to me, questions about the "rightness and wrongness" of inequality have always been central.  Indeed, in many ways, my academic career--and certainly my efforts in helping to develop resource-based theory in the field of strategic management--can be understood as an effort to understand the relationship between these to "theories" of inequality in society--that it is morally bad and that it is both inevitable and can be good.  That I have chosen to confront these issues in the context of business firms is at least partially a matter of chance and good fortune.  I could have chosen to confront these same issues in a very different context, say in the context of the ideological struggle between socialism and capitalism.  Whether we study "Why do some firms outperform others" or "Why do some economic system outperform others," at some level, these are both questions about the causes and consequences of inequality.²

²    My interest was in understanding the causes and consequences in the inequality of outcomes.  In high school, I was less interested in inequality in opportunities since--in my white, middle class high school--inequality in opportunities was not likely to be much of a problem.  However, in retrospect, it seems to me that my high school teachers adopted the same logic that I will describe among SCP scholars--that my heterogeneity in outcomes must reflect heterogeneity in opportunity.  This conclusion only makes sense if people/firms are perfectly homogeneous.

PG.# 285 BARNEY
I included that--at Yale, at least--there was no sociological theory, only a loosely connected set of ideas that were applied to studying a wide variety of disconnected phenomena--the sociology of medicine, the sociology of sport, the sociology of religion.  Sociology had become applied statistics.

A simple story makes this point.  The Ph.D. students in the Sociology Department decided to form a softball team for the graduate school softball tournament.  At the organizing meeting, we had to choose a name of our team.  Here we were, fifteen Ph.D. students in sociology and we couldn't come up with a single uniquely sociological concept which we could use to name our team.  In the end, we decided to call ourselves the "Chi Squares"--we gave up on sociological theory as a source of inspiration and fell back on statistics!⁵

⁵    I personally liked the name proposed by a child of one of my fellow students--"The Swords!"

PG.# 295 BARNEY
And, what is personally satisfying is that resource-based theory really is a theory about inequality in society.  While acknowledging that sometimes inequality in outcomes can be inefficient, even evil, resource-based theory's core message is: heterogeneity in outcomes in society is common and natural and is often good for all of us, those who are advantaged as well as those who are disadvantaged.  If firms are "better off" because they are more skilled at addressing customer needs, then this inequality in outcomes is perfectly consistent with maximizing social welfare in society.

PG.#296 BARNEY I remember meeting with a new Ph.D. student who had arrived on campus early and was interested in getting a head start on his reading.  He came to my office and asked me what he should read.  Following the example of Bill Ouchi, I suggested that he read Williamson's Markets and Hierarchies and come back in a few weeks to talk about it.  The student came back with a forty-page summary of Williamson's arguments that he wanted to give to me.  I thanked him, but declined.  My response to him was, "I know you have read the book and can summarize what's in it.  My only question for you now is--what is missing from the book?"  That was a question this new Ph.D. student had not considered.  A week later, we got together again and had a rousing discussion of what Williamson's book did not cover.

For me, personally, if I had not had an in-depth understanding of the new institutional economics, it would have been very difficult for me to contribute to the development of resource-based theory.  This is the case, even though the connections between these sets of ideas are subtle and complex.¹⁴  Institutional economics provided me with the tools, but more importantly, a way of thinking about problems, that was instrumental in my resource-based work.  But it was what was missing in institutional economics--a rigorous theory of inequality among competing firms--that led me to think more about resource-based logic.

This said, once one understands the literature, the essential task is to learn to ignore that which you have learned.  Prior literature is both a guide and a blinder.  I have found in my own case that knowing the literature too well can actually prevent me from generating new insights.

¹⁴    Indeed, the connection between, say, transactions cost economics and resource-based theory continues to be discussed today.  See, for example, Lieblein and Miller (2003).

PG.# 297 BARNEY
The field of strategic management has become enamored with what I call the "norm of completeness."  This norm suggests that a single paper can develop a new theory, derive specific testable hypotheses from this theory, develop appropriate data and methods to test these hypotheses, report results, and discuss the theoretical implications of these results--all within thirty-two manuscript pages.  This is insane.

Writing papers that meet the norm of completeness generally means that authors have to compromise on some aspect of their paper.  In general, for most of our journals, the part of the paper that gets short shrift is the theory section.  For most empirical work, theory means: Show how your research question is related to a body of previous literature and develop some new hypotheses that typically require no more than a paragraph of justification.  Indeed, it is not too much of an overstatement to say that there is almost no new theory in most empirical papers.

Look at the seminal theoretical papers and books in strategy.  As Bill Ouchi used to say, "The only numbers in these seminal contributions are page numbers."¹⁶  Moving too quickly to traditional empirical tests of theory can doom creative efforts.

¹⁶    The one exception to this assertion may be Kogut's (1991) paper on real options that developed new and very interesting theory but also had empirical tests.

PG. #299 BARNEY
Of course, I am not appalled if the theories we develop happen to have implications for managers and firms.  Indeed, it is not uncommon that the theories developed by strategy scholars have broad managerial implications.  I consider this a "happy accident."  The reason I develop theory is to solve theory problems, not to solve managerial problems.

I recognize that this perspective contradicts some widely held beliefs about the relationship between business scholars and practitioners.  One of those beliefs is that practitioners typically lead scholars--that the best scholarship describes the actions of practitioners and rationalizes these actions relative to theory.  And, it is certainly the case that empirical research assumes that managers have been behaving in ways consistent with a particular theory in order to generate data consistent with theoretical expectations.

However, in my career, I have met very few managers that are also good theorists.  In fact, they are usually quite bad at it.  For example, ask any successful entrepreneur why they are successful, and they will give some version of the following answer: "I worked hard, I took risks, and I surrounded myself with good people."  Go to a failed entrepreneur and ask what happened, and they will say, "I don't know.  I worked hard, I took risks, and I surrounded myself with good people."  Theory suggests that working hard, taking risks, and surrounding yourself with good people are not sufficient for entrepreneurial success.  Indeed, given the role of luck in entrepreneurial endeavors, such attributes may not even be necessary for entrepreneurial success.  However, few entrepreneurs have broad enough experiences to be able to develop this general theory.

Organizational Effectiveness: Its Demise and Re-emergence through Positive Organizational Scholarship
KIM CAMERON

PG. #305 - 307 CAMERON The earliest models of organizational effectiveness emphasized "ideal types," that is, forms of organization that maximized certain attributes.  Weber's (1947) characterization of bureaucracies is the most obvious and well-known example.  This "rational-legal" form of organization was based on rules, equal treatment of all employees, separation of position from person, staffing and promotion based on skills and expertise, specific work standards, and documented work performance.  These principles were translated into dimensions of bureaucracy, including formalization of procedures, specialization of work, standardized practices, and centralization of decision making (Perrow, 1986).

Early applications of the bureaucratic model to the topic of effectiveness proposed that efficiency was the appropriate measure of performance--i.e., avoidance of uncoordinated, wasteful, ambiguous activities.  That is, the more nearly an organization approached the ideal bureaucratic characteristics, the more effective (i.e., efficient) it was.  The more specialized, formalized, standardized, and centralized, the better.

Subsequent scholars challenged these assumptions, however, suggesting that the most effective organizations are actually non-bureaucratic.  Barnard (1938), for example, argued that organizations are cooperative systems at their core.  An effective organization, therefore, channels and directs cooperative processes to accomplish productive outcomes, primarily through institutionalized goals and decision making processes.  Barnard's work led to three additional ideal type approaches to organization--Selznick's (1948) institutional school, Simon's (1956) decision making school, and Roethlisberger and Dickson's (1947) human relations school.  Each of these schools of thought represents an ideal to which organizations should aspire--e.g., shared goals and values, systematic decision processes, or collaborative practices.  Whereas devotees disagreed over what the ideal standard must be for judging effectiveness, all agreed that effectiveness should be measured against an ideal standard represented by the criteria.

Over the years, ideal types proliferated, including goal accomplishment (Price, 1982), congruence (Nadler and Tushman, 1980), social equity (Keeley, 1978), and interpretation systems (Weick and Daft, 1983).  However, mounting frustration over the conflicting claims of ideal type advocates gave rise to a "contingency model" of organizational effectiveness.  This perspective argued that effectiveness is not a function of the extent to which an organization reflects qualities of an ideal profile but, instead, depends on the match between an organization's attributes and its environmental conditions.

Burns and Stalker's (1961) differentiation between organic and mechanistic organizational types represents an early bridge from ideal type to contigency models.  These authors argued that mechanistic organizations (e.g., those reflecting Weber's bureaucratic dimensions) are best suited to highly stable and relatively simple environments.  In contrast, organic organizations (e.g., those reflecting Barnard's cooperative dimensions) are better suited to rapidly changing, highly complex situations.  This idea spawned several significant research programs, all based on a contingency view of effectiveness--Lawrence and Lorsch's (1967) study of multiple industries in which differentiation and integration were predictive of effectiveness, the Aston studies in England (Pugh, Hickson, and Hinings, 1969) in which structural arrangements were predictive of effectiveness, and Van de Ven and Ferry's (1980) development of the Organizational Assessment Survey in which different processes and design features were predictive of effectiveness.  All these studies concluded that evaluations of effectiveness differed depending on environmental circumstances.  Complex and changing environments give rise to different appropriate effectiveness criteria than do stable and undemanding environments.

A third shift occurred in the conception of organizations as economists and organizational theorists became interested in accounting for transactions across organizational boundaries and their interactions with multiple constituencies.  This emphasis highlighted the relevance of multiple stakeholders in accounting for an organization's performance (e.g., Williamson, 1983; Connolly, Conlon, and Deutsch, 1980; Zammuto, 1984).  Effective organizations were viewed as those which had accurate information about the demands and expectations of strategically critical stakeholders and, as a result, adapted internal organizational activities, goals, and strategies to match those demands and expectations.  This viewpoint held that organizations are elastic entities operating in a dynamic force field which pulls the organization's shape and practices in different directions--i.e., molding the organization to the demands of powerful interest groups including stockholders, unions, regulators, competitors, customers, and so forth.  Effectiveness, therefore, is a function of qualities such as learning, adaptability, strategic intent, and responsiveness.

Managerial and Organizational Cognition: Islands of Coherence
ANNE S. HUFF

PG. #332 HUFF The foundation for understanding managerial and organizational cognition (MOC) was laid in the 1980s.  The Thinking Organization (1986), edited by Sims and Gioia, was an important early landmark that showed how management scholars were applying a cognitive perspective to a broad range of management subjects.  I wanted the book I edited, Mapping Strategic Thought (1990), to be the next major landmark.  It provides a hierarchy for organizing work in the field, and ties that organizing framework to a set of available methodologies.  Key concepts from this book and other work I did in the "golden era" of MOC research are summarized in the first part of this chapter.  The second part describes how I moved from thinking about cognition as the central aspect of strategic decision making to making cognition the anchor of a broader attempt to understand strategic action.  This transition is part of a general shift in strategy and organization theory toward dynamic models.  I suggest that we could be entering a new era of enthusiasm for cognitive research because of the requirements of these models.

My research interests and objectives have been informed by others' work, and I am particularly aware of the influence of people at the University of Illinois, one of the important centers of cognitive research (in management and in other fields) in the 1980s.  It is not possible to describe MOC in detail in this chapter, but it is interesting to relate a brief summary of MOC to descriptions of scholarly development from the philosophy of science, which I do toward the end of the chapter.  That leads to some advice for readers in the conclusion.

PG. #345 & 346 HUFF 16.4 LINK TO PHILOSOPHY OF SCIENCE The editors of this book ask that authors relate their own theory building efforts to accounts from the philosophy of science.  I have been particularly influenced by the work of Thomas Kuhn (1970).  It seems obvious to me that Kuhn's emphasis on a "paradigm" as an organizing collection of shared assumptions and practices was strongly influenced by emerging cognitive science.  Furthermore, I believe widespread references to Kuhn in management studies are due at least in part to familiarity with the idea of schematic frameworks.

Most of the observations in this chapter can be put into a Kuhnian framework: Cognitive science as a field was developing a strong paradigm around schema theory in the 1970s.  Work in MOC drew on this source, but was developing its own interests and methods as a subfield in the subsequent decades.  The MOC division in the Academy of Management provided an important forum for regular interaction, and usefully promoted both methodological and theoretical discussions.  Similar but distinctive meetings were being held in Europe, with enough international travel to enrich the worldwide gene pool of research ideas.

My mapping book was an attempt to contribute to theoretic arguments in this field as well as codify tools and methods.  The book was strengthened by knowledge of and discussion of research activities at the University of Illinois, especially in the business school, but also in psychology and other fields.  Other strong centers for cognitive research, especially at New York University, Penn State, Cranfield University, Bath, and Strathclyde provided other hospitable climates.

Although all of this is compatible with Kuhn's account of paradigmatic science, the historical development of MOC also refutes some aspects of his account.  In particular, the development of theory has been less coherent than a reading of Kuhn might suggest.  Many opportunities for sustained conversation, even in the areas of environmental interpretation and competitor analysis where work has been most concentrated, have not fully developed.  In part this seems to be due to a strong desire for independence, which decreases desirable cross-citation, and lures many individuals into new directions before they fully develop their current projects.  Cumulative activity also seems to be weakened by journals that encourage claims of independent discovery.  But neither of these seem to be sufficient explanation.

Developing Theory about the Development of Theory
HENRY MINTZBERG

PG. #355 & 356 MINTZBERG I have no clue how I develop theory.  I don't think about it; I just try to do it.  Indeed, thinking about it could be dangerous:

The centipede was happy quite
Until a toad in fun
Said, "Pray, which leg gores after which?"
That worked her mind to such a pitch,
She lay distracted in a ditch
Considering how to run.
(Mrs. Edward Craster, 1871)

I have no desire to lay distracted in a ditch considering how to develop theory.  Besides, that's the work of cognitive psychologists, who study concept attainment, pattern recognition, and the like, but never really tell us much about how we think.  Nonetheless, I'll take the bait, this once, at the request of the editors of this book, because I probably won't get far either.

I want to start with what theory isn't and then go on to what theory development isn't, for me at least, before turning, very tentatively, to what they seem to be.

17.1 WHAT THEORY ISN'T: TRUE It is important to realize, at the outset, that all theories are false.  They are, after all, just words and symbols on pieces of paper, about the reality they purport to describe; they are not that reality.  So they simplify it.  This means we must choose our theories according to how useful they are, not how true they are.  A simple example will explain.

In 1492, we discovered truth.  The earth is round, not flat.  Or did we?  Is it?

To make this discovery, Columbus sailed on the sea.  Did the builders of his ships, or at least subsequent ones, correct for the curvature of the sea?  I suspect not; to this day, the flat earth theory works perfectly well for the building of ships.

But not for the sailing of ships.  Here the round earth theory works much better.  Otherwise, we would not have heard from Columbus again.  Actually that theory is not true either, as a trip to Switzerland will quickly show.  It is no coincidence that is was not a Swiss who came up with the round earth theory.  Switzerland is the land of the bumpy earth theory, also quite accurate--there.  Finally, even considered overall, say from a satellite, the earth is not round; it bulges at the equator (although what to do with this theory I'm not sure).

If the earth isn't quite round or flat or even even, then how can we expect any other theory to be true?  Donald Hebb, the renowned psychologist, resolved this problem quite nicely: "A good theory is one that holds together long enough to get you to a better theory."

But as our examples just made clear, the next theory is often not better so much as more useful for another application.  For example, we probably still use Newton's physics far more than that of Einstein.  This is what makes fashion in the social sciences so dysfunctional, whether the economists' current obsession with free markets or the psychologists' earlier captivation with behavioralism.  So much effort about arm's lengths and salivating dogs.  Theory itself may be neutral, but the promotion of any one theory as truth is dogma, and that stops thinking in favor of indoctrination.

So we need all kinds of theories--the more, the better.  As researchers, scholars, and teachers, our obligation is to stimulate thinking, and a good way to do that is to offer alternate theories--multiple explanations of the same phenomena.  Our students and readers should leave our classrooms and publications pondering, wondering, thinking--not knowing.

PG. #358 & 359 MINTZBERG But it does so much of the time, because we confuse rigor with relevance, and deduction with induction.  Indeed the proposal I received for this very book did that: "...the process of theory building and testing is objective and enjoys a self-correcting characteristic that is unique to science.  Thus the checks and balances involved in the development and testing of theory are so conceived and used that they control and verify knowledge development in an objective manner independent of the scientist."  They sure do: that is why we see so little induction in our field, the creation of so little interesting theory.

Kark Popper, whose name a secretary of mine once mistyped as "Propper," wrote a whole book about The Logic of Scientific Discovery (1959).  In the first four pages (27-30), in a section entitled "The Problem of Induction," he dismissed this process, or more exactly what he called, oxymoronically, "inductive logic."  Yet with regard to theory development itself, he came out much as I did above.

The initial stage, the act of conceiving or inventing a theory, seems to me neither to call for logic analysis not to be susceptible of it.  The question how it happens that a new idea occurs to a man--whether it is a musical theme, a dramatic conflict, or a scientific theory--may be of great interest to empirical psychology; but it is irrelevant to the logical analysis of scientific knowledge.  This latter is concerned not with questions of fact (Kant's quid facti?), but only with questions of justification or validity (Kant's quid juris?)...Accordingly, I shall distinguish sharply between the process of conceiving a new idea, and the methods and results of examining it logically.  (Popper, 1959: 31)

Fair enough.  But why, when he devoted the