Theory in the organizational sciences

Abstract

In this essay, we further delineate the defining characteristics of theory as well as what constitutes a theoretical contribution in organizational research cultivated by our collective experiences in the field. Additionally, we offer our views regarding the fragmented state of thinking that currently exists, how this view has come about, as well as available remedies. Unfortunately, an accurate and honest treatment requires the realization that many of the problems facing the field are not likely be solved without radical shifts in its philosophy. In our identification of issues and subsequent discussions, we err on the side of candor, which may offend some readers. Others may simply view our beliefs as unduly cynical. However, our intention throughout this essay is merely to “call-em-like-we-see-em” and not to overstate the case or elicit strong emotions or negative reactions. On the other hand, we view it as a disservice to simply reiterate the “party line,” which presents an existing knowledge base that is both robust and accommodating. Clearly, it is neither.

Keywords

ambiguity organizational sciences theory theory development

“If the facts don’t fit the theory, change the facts.”

Albert Einstein

It is no exaggeration that theory serves as the foundation of the organizational sciences. Unfortunately, there are few issues in the field that have generated more confusion and disagreement among scholars than “what constitutes theory?” (e.g., Corley & Gioia, 2011; Reay & Whetten, 2011; Shapira, in press; Sutton & Staw, 1995). Undeniably, interrater agreement on what constitutes theory, and what does not, hovers around the same pitifully low level as does interreviewer agreement found in the journal review process (Bedeian, 2003; Tsang & Frey, 2007). Although phrases such as “dust-bowl empiricism at its dustiest” and “theoretically vacuous” call to mind papers that are virtually devoid of theory, we have few commonly agreed upon principles to guide the development of scholarship (e.g., Corley & Gioia, 2011; Oswick, Fleming, & Hanlon, 2011).

As a consequence, this documented confusion has generated considerable frustration for scholars who find that “lack of sufficiently well-developed theoretical foundation” represents an all-too-frequent rationale for manuscript rejection. Collective ambiguity regarding theory is, in part, why the editor of Organizational Psychology Review has decided to focus scholarly attention on this important but not well-understood issue (indeed, the first such essay was published in the first issue of the journal; van Knippenberg, 2011). We hope that we can provide insights into problems and opportunities associated with theory development drawn from our collective 9 decades of experience in the field.

The nature of theory in the organizational sciences

With its intellectual foundations going back over a century (e.g., Dewey, 1896; James, 1907), and drawn from the fields of psychology, sociology, political science, and economics, the organizational sciences reflect a collective body of knowledge that is inherently expansive (Buckley, Hamdani, Klotz, & Valcea, 2011; Ferris, Ketchen, & Buckley, 2008). Over the years, the discipline has expanded to include broad and diverse areas that include organizational behavior, organizational theory, human resources management, and strategic management, and their multidisciplinary roots. Thus, it has been no small or insignificant task to communally develop theoretical explanation to drive empirical research.

Without recognized theory development, science is unable to separate or bring together phenomena, which is a requisite characteristic in the formation of a collective body of knowledge (Strong, Jeanneret, McPhail, Blakley, & D’Egidio, 1999). Indeed, any scientific field of inquiry requires sound theory development, because it serves as the basis for testing ideas and gaining new insights, which allows for the natural process of theory validation or disconfirmation to occur.

Because of the lack of agreement regarding theory, scholars have sought uniform guidelines that everyone could follow, essentially taking a highly subjective, interpretive phenomenon and transforming it into an air-tight, objective entity with no misinterpretation (Dubin, 1976; Gray & Cooper, 2010). Unfortunately, although we can provide more substance and definition (and, in fact, we hope to help a bit with that issue in this essay), the ultimate determination of what constitutes good theory (or a worthy theoretical contribution) is made through persuasive argumentation and subsequent affirmation, not by any sort of objective litmus test. Foundationally, it is difficult to develop a shared appreciation for theory when scholars are unable to agree upon its definition. Samples, which illustrate definitional similarities and differences, are provided below:

“A systematic statement of principles involved; a formulation of apparent relationships or underlying principles of certain observed phenomenon which has been verified to some degree” (Webster’s New World College Dictionary, 1997).

“A statement of relations among concepts within a set of boundary assumptions and constraints. It is no more than a linguistic device used to organize a complex empirical world” (Bacharach, 1989, p. 496).

“The attempt of man to model some theoretical aspect of the real world” (Dubin, 1976, p. 26).

“The formation of testable hypotheses” (Gorelick, 2011, p. 1).

“Theory is a statement of concepts and their interrelationships that shows how and/or why a phenomenon occurs” (Corley & Gioia, 2011, p. 12; Gioia & Pitre, 1990).

“A theory is a set of assumptions and the causal logic that explains the relationships among the constructs (not variables)” (Combs, 2010).

Accordingly, the definitions noted above reflect a representative sampling of the scope and range of definitions of theory in the field to date, thus indeed demonstrating considerable variability in how theory is construed (Leavitt, Mitchell, & Peterson, 2010). Yet, there do appear to be some commonalities across some of the definitions, permitting us to extract, perhaps, as close to a generally agreed-upon way to characterize theory in the organizational sciences. As a result, we might generally agree that theory represents a systematic explanatory statement about the relationships among a set of constructs, with accompanying logic and assumptions. So, theory has explanation as its defining principle, albeit formal and systematic.

Finding or developing “good” theory: Toward the interplay between theory and method

Over the years, scholars have debated the characteristics of good theory and/or theoretical contribution in both formal and informal academic settings. Because scrutiny ultimately gauges the legitimacy of any theory, methodological appropriateness is obligatory. Although widely assumed as both a necessary and sufficient condition, development remains affected by the incompatible theory–method situation (Mintzberg, 2005). Weick (1989) argued that theories frequently are developed because they are particularly accessible to methodological validation, such as replications and tests of theoretical extensions. In support, van Maanen, Sorensen, and Mitchell (2007) argued in favor of the strong theory–method exchange. Leavitt et al. (2010) argued that “problems that emerge in theory development and empirical testing may be highly cyclical” indicating at least moderate reciprocal influence.

However, this pursuit of acceptable theory–method interplay has fallen short of its intended objective. Instead, these largely avoidable recurrences have promoted the acceptance of findings from single, uncorroborated studies as fact rather than the first step in the knowledge-generation process (Tsang & Kwan, 1999). Despite the historically strong support for research focusing on replication or incremental extension studies that promote theory development and refinement (Hochwarter, Ferris, & Hanes, 2011), a disturbing trend has emerged in recent years.

McKinley (2010) proposed that the organizational sciences have become unbalanced with respect to the activities of theory development and theory testing in recent years. This reality is not new, but has been in progress for a number of years. Friedman (1949, p. 489) wrote that “we curtsy to Marshall but we walk with Walras.” Followers of Marshall were noted for not straying far from their data, while followers of Walras fervently believed that theory and its development was the primary goal of research. Walrasians further believed that empirical reality needed to be explained theoretically before any empirical investigations were undertaken. Apparently, our field has been overwhelmed by Walrasians.

Specifically, the development of theory appears to have become the ultimate goal in the organizational sciences (e.g., Hambrick, 2007), resulting in activities fundamental to traditional scientific advancement (i.e., theory testing and empirical replications of proposed relationships; Kuhn, 1970) becoming seriously neglected. Specifically, McKinley (2010) argued that scholars now view theory development as the fundamental goal of science rather than “a means to further ends” (p. 48). As a result of this shift in focus, scholars have distanced themselves from the activities that are required to establish the validity status of theory. Furthermore, recently some scholars have suggested that top journals in the field (e.g., Academy of Management Review) seem to be expressing a strong preference for publishing only “revelatory contributions to theory” and not “incremental contributions to theory” (Corley & Gioia, 2011). In the next sections, we discuss what we see as some of the problems in the current system, and propose suggestions for changing the existing state of affairs.

Is the organizational research system broken?

Organizational science research operates within a system that often obscures true knowledge generation. Nontraditional ideas with the potential to provoke thought and redirection often suffer from overt denunciation with little opportunity for further discussion (Cummings & Frost, 1995; Staw, 1995). More understated, yet equally impactful is the increasingly disorganized state of management theory (e.g., Albert & Anderson, 2010). Scholars have maintained that construct redundancy, a practice of repackaging older constructs with newer labels, has contributed to the fragmentary state of management theory (Colquitt & Zapata-Phelan, 2007; Spell, 2001). Below, we note and discuss some of the contributing factors, which observably share varying degrees of overlap.

Requiring “revelatory contributions” to theory

The requirement that we must produce “revelatory contributions to theory” in order to develop acceptable work for premier publication outlets is one that has been detrimental to the advancement of knowledge in our profession (Hambrick, 2007). In definitional terms, revelatory contributions have an element of surprise as an important component (Corley & Gioia, 2011; Mintzberg, 2005). This view is best articulated by Davis (1971) who argued that “The best way to make a name for oneself in an intellectual discipline is to be interesting - denying the assumed, while affirming the unanticipated” (p. 343). In our haste to only acknowledge theoretical contributions that are novel and direction-altering, we have committed a major blunder in a number of ways. For one thing, by implication, this preoccupation with revelatory contributions to theory seriously marginalizes the nature of incremental contributions, which are very important to theory development, and always have been.

Additionally, what is missing from our development strategies are the pruning efforts that would result in parsimony and a healthier organizational science (Leavitt et al., 2010). Indisputably, we are in the process of inundating ourselves with “revelatory contributions to theory.” Think of this from a Malthusian perspective. We are geometrically increasing theory in the absence of arithmetically pruning existing theory. We are in the process of creating a situation whereby in order to know anything, we must know everything—certainly an untenable requirement for the advancement of knowledge in the organizational sciences.

One of the most important realities of our profession is that we need to demonstrate our ability to publish in the premier journals in our field. Let’s take the case of the Academy of Management Review (AMR). Publishing in this journal helps one earn their spurs in our profession. Ask any doctoral student about their goals, and one of them invariably is to publish an article in AMR. Undoubtedly, AMR is a very good journal with unquestioned consensus that its contributions to science have been considerable. Interestingly though, an analysis by Halbesleben, Wheeler, and Buckley (2004) revealed that the overwhelming majority of contributions to the AMR failed to generate any follow-up, much less an effort to critically analyze or prune the theory which was suggested in the journal.

As further evidence, Corley and Gioia (2011) identified few instances where the year’s best paper was the one subsequently most cited. Given this outcome, we must conclude that while the AMR has generated a significant amount of thought, it has generated a negligible amount of knowledge in the organizational sciences. In spite of this, establishing academic credentials dictates that the AMR will never suffer from a dearth of contributions intended to push the frontiers of our knowledge.

Because the development of theory has become the ultimate goal in the organizational sciences (e.g., Hambrick, 2007; McKinley, 2010), theory testing apparently has been relegated to an inferior role, as an unimportant and nonrewarded activity. Eden (2004) lamented about what it takes to get an article accepted for publication in the Academy of Management Journal (AMJ), with particular reference to revelatory theory contributions. He concluded that if you tested a theory published in AMR, and submitted it to AMJ for review, it would be considered unacceptable, because it is not viewed as making an important enough contribution to theory. He concluded, and we wholeheartedly agree, that this is absolutely ridiculous! Theory testing is a contribution to theory (McKinley, 2010), as are tests of theories in different contexts, which have been labeled by some scholars as merely incremental contributions (i.e., as opposed to theory development revolutionary contributions), and thus probably not acceptable for publication in top journals.

The whole idea of “revelatory contributions to theory” has become a crutch in our field, and the easy way for reviewers to reject an otherwise competently done and insightful piece of work. The process becomes even more intricate and potentially flawed as a function of who makes the judgment of what constitutes a revelatory contribution, and can that person really make that judgment objectively and without bias? What if a paper submitted to a journal for review, which proposes a new theoretical development, is sent to a reviewer who has published a competing theory in that area? Is it possible for this reviewer to provide an unbiased evaluation of this contribution? It does not seem so, but this happens more frequently than likely confessed.

We ask our readers, were you consulted about this move toward “revelatory contributions to theory” as a criterion for publication in our major journals, and as the best way to advance the field? We thought not! Let’s take an example from a number of years ago. Phenomenon A is shown in a research study to elucidate many differences between those who experience it and those who do not. Subsequent researchers have been unable to replicate those conditions surrounding Phenomenon A. However, with the first-mover advantage, and the idea that demonstrating that the null hypothesis is true is not probative (i.e., nor typically publishable), many still believe Phenomenon A is a potent intervention.

This is partially due to our insistence upon “revelatory contributions to theory” as a prerequisite for publication. Are we the only individuals who think that this condition may have been instrumental in stunting advances toward knowledge generation? We bet not! We seem to have forgotten what Einstein said: “Not everything that can be counted counts, and not everything that counts can be counted.” There is more than one way to make a contribution to what we know! We are unaware of any scholarly discipline that has reviewer/editor “shock, awe, and hyperventilation” as evaluative dimensions.

Obstructions to theory clarification

The perception process

Lewin (1936) suggested that we operate on our perceptions of reality, not reality per se, and at best, we hope that the two are at least moderately related (i.e., reality vs. our perceptions of it). However, we do know some things about the perception process that might be useful here in developing a better understanding of the problematic status of theory. With little doubt, scholars certainly view theory, and what constitutes a theoretical contribution, quite differently. Indeed, we have seen instances where two or more reviewers reading the same paper, will articulate very different evaluations of the development of the theory serving as the foundation of the paper (i.e., in one extreme case, one reviewer said the framework indeed represented sound theory, and another reviewer said it was not theory at all). Also, what individuals perceive to be the case is strongly influenced by their own experiences, attitudes, and biases. Thus, one scholar’s evaluation of the theoretical development in a reviewed paper will most likely be influenced by the reviewer’s own research in a related area, and the theoretical development which the field has acknowledged.

Additionally, what a scholar reviewing a paper sees/perceives (i.e., in terms of value, quality, or contribution) will be influenced by the mindset or perspective regarding what he sees as his goal or objective in doing the review. That is, years ago, reviewers were more willing to search harder for potential contributions than simply conclude that the manuscript needed significant work (i.e., outright rejection). If the reviewer saw a “diamond in the rough” that could be developed into a publishable manuscript, taking a development was the norm rather than the exception (i.e., revise and resubmit with substantive recommendations). There seems to be much less of this approach today, and it could have to do with the perspective changing from “seeking good papers to publish,” to a search for negative elements with papers getting accepted only because not enough wrong things could be found. It sounds like we are talking about the same outcome, but the mindset reviewers take to get there are quite different in nature.

Errors of omission

It is apparent that some scholars feel little need for clarification regarding theory and theoretical development in the field because they honestly feel none is needed. Instead, it is presumed that the nature of what is good theory is something we have all known well since graduate school. There is no doubt that scholars differ in their understanding of theory development, with experienced theoreticians (e.g., Weick, Whetten, etc.) much more comfortable rendering evaluations of theory. Others may struggle more with the inherent ambiguity of theory development, and are perhaps not sure if they will know it when they see it.

Furthermore, we have written elsewhere about the nature of graduate school training in both theory and methods, and there is clear evidence that it is unbalanced in favor of methods and statistics and short-changing theory building. Also, within this focus, teaching and practice favor linear approaches to both theory and methods in the organizational sciences (Ferris et al., 2006; Ferris, Perrewé, & Buckley, 2009). Recent evidence exists advocating a more expansive view of organizational phenomena (Hochwarter, Ferris, Laird, Treadway, & Gallagher, 2010; Zellars, Hochwarter, Lanivich, Perrewé, & Ferris, 2011).

Errors of commission

An alternative perspective on the lack of clarity in theory development is that it is, in some sense, intentional, and a group of scholars in the field prefer to keep the ambiguity surrounding the nature of theory because it serves important purposes for the field. We would argue that the primary purpose it serves well is to give journal editors, associate editors, and reviewers a very convenient and defensible rationale for rejecting articles, thus allowing them to maintain the selectivity and high rejection rates. More so today than ever before, the top journals require that articles accepted for publication make a significant contribution to theory, as well as being firmly grounded in a well-articulated theoretical foundation.

Yet, what constitutes a significant theoretical contribution is highly subjective, which is why “lack of a theoretical contribution” has become the most commonly employed reason for article rejection. However, because a “theoretical contribution” remains so ambiguous, arguing against such a rejection decision becomes virtually impossible. Thus, as long as theory issues continue to serve such defining purposes, clarification will never be seen as an important objective to be attained by many scholars in the field.

Can it be fixed?

Hambrick (2007) has suggested that we should not abandon this whole theory thing; that is, even though we may have just gone overboard with it and it is causing a lot of problems, we should find a way to fix it. We tend to think he is probably right (mostly). So, what can be done? It seems that we can go in one of two directions. One is to keep the system the same, make no changes, and just live with it and assume that all will work out in the end. We are not optimistic that this passive approach will ameliorate the problems that currently exist. The trend line, which continues along a sustained negative path, does not champion the “letting it run its course” option.

A second approach would be to arrive at the obvious conclusion that we have a system in dire need of major overhaul. In light of the confusion it causes, it might make sense to replace discussions of “theory” with language more conducive to advancing science; for example, we could replace “theoretical contribution” with “logical arguments that support and extend the existing research base.” Thus, more or less start from scratch, and build a collective and shared understanding of the terms and processes.

Another idea might be to encourage more interaction between editors and authors regarding “theoretical deficiencies.” Why? What is needed? It did not make a compelling case for what reasons? Rejecting a submitted paper by simply stating that it failed to make a significant contribution to theory is easy, but it does not help in building a developmental understanding so that the authors might be more successful next time around. Same goes for reviewers—developmental reviews are always more healthy. Good reviews are much better than quick reviews, and editors frequently reward those who get them done in a timely manner, not always the best-quality reviews.

Contributions to theory examples

In the following sections, we try to provide some ideas regarding what we see as good theory and/or contributions to theory in the field today (Corley & Gioia, 2011). In essence, we cast the net a bit more widely than some scholars, but believe such an approach ultimately will better serve scientific advancement in the organizational sciences.

Theory development from “novel theoretical insights” and “combining lenses”

Ferris et al. (2007) proposed an agentic theory of social/political influence in organizations, which focused on the political skill construct, and how it influenced the management of shared meaning (i.e., utilizing the influence/politics definition proposed by Ferris and Judge [1991]). The word “agency” suggests intentional activity, and theories of human agency characterize individuals, not simply passive reactors to, but rather as active creators of their environments (Bandura, 2006).

Thus, Ferris et al.’s (2007) theoretical approach was developed from “novel theoretical insights from reviews of existing theory and research,” as suggested recently by LePine and Wilcox-King (2010) as a legitimate way to develop theory in the organizational sciences. A special case of this approach recently has been discussed by Okhuysen and Bonardi (2011), and referred to as “building theory through combining lenses.” They suggested that this process involves developing new insights and essentially building new theory through the use of combinations of ideas or perspectives in the field.

Previous theory in this area identified and discussed the types of influence approaches, but none explained the situational savvy contributing to the selection of the proper techniques, and the actual execution of influence in ways that led to effectiveness. Jones (1990) referred to these areas as the interactive style component, suggested that it largely explained the success or failure of influence attempts, and he argued that we had little understanding of it, thus, leaving a large part of social influence unexplained. Therefore, the Ferris et al.’s (2007) conceptualization helped to address some important gaps in our understanding of social and political influence in organizations.

Theoretical contribution through contrasting theory testing

Hochwarter et al. (2006) conducted an investigation of understanding as a moderator of the relationship between organizational politics perceptions and job performance. They argued that there are two competing theories or perspectives regarding how understanding affects the politics perceptions–job performance relationship (i.e., the antidote hypothesis vs. the distraction hypothesis), and they pitted these two explanations against each other in a competitive test conducted in three separate samples. The argument for the antidote hypothesis suggests that increased understanding reduces or neutralizes the potentially negative effects of politics perceptions (i.e., as a work environment stressor) on job performance by reducing perceptions of ambiguity. On the other hand, the argument for the distraction hypothesis suggests that increased understanding in political environments may make salient and thus direct individuals’ attention to politics and less on job tasks, thus serving as a distracting function, which tends to exacerbate politics’ negative effects on job performance.

Therefore, this investigation examined whether increased understanding provides individuals with increased clarity and information that improves task performance (i.e., the antidote effect), or distracts workers from job tasks, which serves to decrease job performance (i.e., distraction effect). In so doing, this investigation competitively pitted two different yet theoretically grounded and logically compelling perspectives concerning the operation of the politics perceptions–understanding interaction on job performance against one another in a fair competition in a “strong inference” framework (Platt, 1964), in order to see which was supported. Furthermore, the analyses were repeated in two additional samples to see if the results from the first sample investigation would “constructively replicate” in the other samples (Lykken, 1968). The results demonstrated support for the distraction hypothesis in Sample 1, and those results were replicated in Samples 2 and 3. Therefore, this research makes interesting and important contributions to theory in this area.

Context, conceptual extensions, and multistudy packages as contributions to theory

Although there have been appeals for greater consideration of contextual effects in organizational research, such appeals unfortunately have been largely ignored when developing theory and research in the field (Johns, 2006; Whetten, 2009). However, such lack of consideration for the role of context can perpetuate incomplete or erroneous conclusions from organizational research. Because of the often ambiguous nature of work environments, the accurate interpretation of phenomena under investigation can be substantially influenced. Thus, research needs to be conducted in varying contexts to be able to accurately assess whether results are context specific, or they transcend contexts (Eden, 2004).

Meta-analyses and replications are intricately connected, because both serve as metrics to assess accumulations of single-study investigations (e.g., Eden, 2002). Thus, because meta-analysis is not a viable tool to assess consistency across studies when few commonalities exist across investigations, primary research studies and replications are extremely critical to continue in the field (Aguinis, Pierce, Bosco, Dalton, & Dalton, 2011; Eden, 2002). So, both meta-analysis and replications of research are important tools which can contribute to scholarly benefits of theory testing, confirmation, extension, and/or the development of new theory (Aguinis et al., 2011).

Additionally, Hochwarter et al. (2011) have added “multi-study research packages” to meta-analyses and replications as complementary mechanisms of theory and research advancement. Such research packages frequently employ multiple methodologies and theoretical explanations, involve more than one study arranged within a single article, and thus allow for increased recognition of the “interplay between theory and method” (van Maanen et al., 2007). Hochwarter et al. (2011) discussed how multistudy packages can make important contributions to theory, whereby, for example, theory extensions that are empirically supported can extend the initial theory tests if results generalize to other time periods, contexts, and/or populations.

Meaningful incrementalism

In recent years, considerable discussion has centered on the threshold level of originality needed for a theoretical contribution to be recognized (Eden, 2010; Tsui, 2009). Without question, revelatory contributions are encouraged and supported with significantly more vigor than their incremental counterparts (Corley & Gioia, 2011; Pfeffer & Sutton, 2006). This reality, which often casts incremental contributions as trivial and space-absorbing, has been nurtured despite the fact that modest contributions tend to drive empirical research at a much higher rate that those deemed more prodigious.

In terms of explaining this focus, we suggest that ego explains at least a modest level of unexplained variance. Specifically, the label of being the editor who failed to present their field path-breaking, thought-changing, and science-expanding theory is not typically sought by accomplished scholars. Moreover, we see this emphasis as having less to do with science and more with editors’ interest in “out-smarting the smart guys,” which occurs with the presentation of state-of-the-art ideas previously unconsidered.

Building on these realities, we contend that not all incremental contributions are equal. We similarly argue that revelatory contributions can regressively serve science by discounting the cumulative, positive influence of those considered incremental. For any theory to impact science, whether it’s incremental or revelatory, a number of factors warrant consideration. First, the theory must allow science to view a particular phenomenon from a unique lens (i.e., perspective). Second, the theory must elicit a “that’s interesting” reaction (i.e., provocation). Third, the theory must have legitimate foundational underpinnings (i.e., presumption) that support its tenets. Fourth, the theory must be amenable to evaluation for refutation or endorsement (i.e., proving). Fifth, theory evaluation must be feasible in terms of both scholar and organizational resources (i.e., prudent). Sixth, theory must be cross-disciplinary and serve multiple contexts (i.e., permeating). Finally, the theory must facilitate subsequent refinement and empirical testing (i.e., promotion). It is hoped that adherence to this list will help ward off the “theory development for theory’s sake” criticism that pervades the organizational sciences.

In presenting the previous list of conditions, our intention was to provide a roadmap rather than a calculator as it is inconceivable that each of the “seven Ps” would be weighted equally. Despite this admonition, we maintain that scholars strongly consider this outline when submitting theoretical manuscripts for publication. We advocate that reviewers and editors contemplate attention to these requirements during the evaluation process.

Conclusion

We have succeeded in placing a hopeless burden on researchers—producing “revelatory contributions to theory.” We are left wondering how Thomas Kuhn would respond to this criterion, given that he thought that the progression of normal science was constructed by slowly establishing detail in accord with existing theory. Hopefully, the Walrasians who have come to dominate our journals (and our field) will not forget Occam’s razor—when given competing theories, we should tend toward the simpler theory! Where we are now is an uncomfortable spot—we have broadened the base of theory in the organizational sciences without a commensurate increase in explanatory power, or what we know about how people behave in organizations.

Footnotes

This research received no specific grant from any funding agency in the public, commercial, or not-for-profit sectors.

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