Identify a Conceptual or Theoretical Framework

BUILDING THEORY ABOUT THEORY BUILDING: WHAT CONSTITUTES A

THEORETICAL CONTRIBUTION?

KEVIN G. CORLEY Arizona State University

DENNIS A. GIOIA The Pennsylvania State University

We distill existing literature on theoretical contribution into two dimensions, origi- nality (incremental or revelatory) and utility (scientific or practical). We argue for a revision in the way scholars approach the utility dimension by calling for a view of theorizing that would enable theories with more “scope” (both scientific and practical utility). We also argue for an orientation toward “prescience” as a way of achieving scope and fulfilling our scholarly role of facilitating organizational and societal adaptiveness.

Theory is the currency of our scholarly realm, even if there are some misgivings about a possible overemphasis on theory building in organization and management studies (Hambrick, 2007). Every top-tier man- agement journal requires a “theoretical contri- bution” before a manuscript will be consid- ered for publication. This tenet is perhaps most strongly felt in this journal, the Academy of Management’s premier conceptual journal (and also, not inconsequentially, the most cited journal in organization studies [based on Web of Science� Journal Citation Reports� data for 2009]). Consistent with this concern, the Academy of Management Review (AMR) has published two special issues dedicated to theory building (1989, issue 4, and 1999, issue 4) and numerous “Editor’s Comments” dedi- cated to trying to articulate what constitutes either theory (e.g., Brief, 2003; Conlon, 2002) or a theoretical contribution (e.g., Kilduff, 2006; Whetten, 1990). These writings, however, de- spite their thoughtfulness, do not represent comprehensive treatments, especially of the latter issue, and do not seem to have hit the mark in a way that provides a satisfactory

resolution to the crucial question of what makes for a theoretical contribution. Thus, scholars are still trying to articulate what it means to make a theoretical contribution (Bar- tunek, Rynes, & Ireland, 2006; Kilduff, 2006; Rindova, 2008; Smith & Hitt, 2005).

A question that typically arises at this point is “What is theory?” Although there are many an- swers to this question, there is little agreement on a universal definition—to wit, “Lack of con- sensus on exactly what theory is may explain why it is so difficult to develop strong theory in the behavioral sciences” (Sutton & Staw, 1995: 372). For our purposes we use a simple, general definition: theory is a statement of concepts and their interrelationships that shows how and/or why a phenomenon occurs (cf. Gioia & Pitre, 1990). We believe, however, that a more pro- ductive question to ask, and for us to address, is “What is a theoretical contribution?” That is, what signifies a significant theoretical (as op- posed to an empirical or a methodological) advancement in our understanding of a phenomenon?

Part of the difficulty in delineating the elusive concept of theoretical contribution is that orga- nization and management studies is an eclectic field—and one with multiple stakeholders as well. Not only do we self-identify as “borrowers” from many other scientific disciplines (e.g., psy- chology, sociology, economics, etc.) but we also claim to speak to both academics and practition- ers. This medley of foundations, voices, and au-

We offer a heartfelt thanks to Blake Ashforth, Don Ham- brick, Trevis Certo, Don Lange, Glen Kreiner, and our anon- ymous reviewers for their helpful comments and critiques on earlier versions of this paper. We especially acknowledge Amy Hillman for her encouragement, commentary, and ex- cellent guidance throughout the revision process.

� Academy of Management Review 2011, Vol. 36, No. 1, 12–32.

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diences often creates confusion when discuss- ing contributions. What exactly is the consensual basis for claiming and assessing theoretical contribution? More pointedly, is there a consensual basis for declaring whether a theoretical contribution exists? One basis for arguing that our field has vague or inadequate standards for assessing theoretical contribution arises from comparing the list of AMR’s Best Articles (awarded one year after publication) with the list of each year’s most cited AMR paper over the same years (based on Web of Science� Social Sciences Citation Index� and/or Google Scholar counts). In only four of the last eighteen years does the paper currently most cited also turn out to be the one chosen as the AMR Best Article for its year of publication (see Table 1), despite the “competitive advantage” in citations such articles have from their publicity for win- ning the award in the first place. This somewhat disconcerting statistic seems to imply some dis- crepancy in assessing a paper’s value right af- ter publication and its value in the future.

As scholars familiar with the practice of de- veloping theoretical contributions, we believe the time is right for our field to turn a reflective lens on itself and try to establish more clearly not only what currently constitutes a theoretical contribution but also, and perhaps more impor- tant, what should constitute a theoretical contri- bution in the future. To help accomplish the first and set the stage for the second, we established two goals for this paper. First, we hope to con- tribute to the practice of making a contribution to theory as it currently stands. Toward this end, we provide a synthesis of the dimensions cur- rently used to justify the existence of a theoret- ical contribution and provide some perspective on the usefulness of these dimensions. Our syn- thesis reveals two dimensions—originality and utility—that currently dominate considerations of theoretical contribution. We also note two subcategories underlying each of these main dimensions, which provide a more nuanced de- scription of the current craft of contributing to theory.

Second, we hope to contribute to what we might call the theory of theoretical contribu- tion—to build theory about theory building, if you will. Thus, we use our synthesis of the liter- ature, as well as our reading of AMR’s Best Ar- ticles and most cited papers listed in Table 1, as

a point of departure for outlining the need for a renewed and reframed emphasis on practice- oriented utility as a focus for future theorizing. In addition, we call for and encourage organiza- tion scholars to adopt an orientation toward pre- science in their theorizing. We define prescience as the process of discerning or anticipating what we need to know and, equally important, of influencing the intellectual framing and dia- logue about what we need to know. An orienta- tion toward prescience holds some promise for advancing our craft of theory development, as well as enhancing the receptivity of the audi- ences for our developing theories beyond the academy and, therefore, conferring a greater po- tential for influencing the organizations and so- cieties we study.

We structure the rest of the article around these two issues. We begin with a synthesis of the theoretical contribution literature as it per- tains to the field of management and organiza- tion studies, highlighting the current state of the art for making a contribution to theory in our top-tier management journals. Building on this synthesis, we then argue that a practice per- spective on theory building would lead to our theories having greater scope and, furthermore, that an orientation toward prescience would en- hance the value and impact of our theoretical contributions. Finally, we discuss implications of our proposals for the field.

SYNTHESIZING CURRENT VIEWS ON “WHAT CONSTITUTES A

THEORETICAL CONTRIBUTION”

Despite the relatively short time that organi- zation and management studies has existed as a field, there is actually quite a collection of writings on the notion of theoretical contribu- tion. We use the term writings because much of this literature is found in editorial statements published in AMR and AMJ. Although there are a number of other sources outside AMR that pro- vide opinion and insight, because AMR is our field’s premier theory journal, much of what fol- lows stems from these writings about making a contribution to theory. In its inaugural (1976) is- sue, for instance, AMR’s “Suggestions for Con- tributors” provided a vision for the types of pa- pers the Academy of Management’s leadership saw as most appealing for the new journal:

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The Review publishes distinguished original manuscripts which (a) move theoretical concep- tualization forward in the field of management, and/or (b) indicate new theoretical linkages that

have rich potential for theory and research in management, and (c) provide clear implications of theory for problem-solving in administrative and organizational situations.

TABLE 1 AMR Best Articles and Most Cited Papers: 1990 –2008 (Citation Counts As of April 2010)

Year Props Volume (Issue) Author(s) Google SSCI Rank

1990 Best Article 15(2) Dollinger 79 16 23rd Most cited 15(1) Reed & DeFillippi 1424 455

1991 Best Article 16(1) Oliver 2213 650 1st Most cited Same

1992 Best Article 17(4) Treviño 113 70 19th Most cited 17(2) Gist & Mitchell 1030 255

1993 Best Article 18(4) Pfeffer 604 305 4th Most cited (Google) 18(2) Woodman, Sawyer, & Griffin 920 311 Most cited (Social Sciences

Citation Index) 18(4) Cordes & Dougherty 866 343

1994 Best Article 19(1) Kahn & Kram 49 20 23rd Most cited 19(1) Ring & Van de Ven 2247 636

1995 Best Article 20(3) Van de Ven & Poole 1132 308 4th Most cited 20(3) Mayer, Davis, & Schoorman 4014 1234

1996 Best Article 21(1) Chen 468 161 10th Most cited 21(1) Lumpkin & Dess 1662 407

1997 Best Article 22(2) Gresov & Drazin 172 54 20th Most cited 22(4) Mitchell, Agle, & Wood 2152 499

1998 Best Article 23(2) Nahapiet & Ghoshal 4106 1080 1st Most cited Same

1999 Best Article 24(1) McGrath 462 151 8th Most cited 24(3) Crossan, Lane, & White 1272 306

2000 Best Article 25(4) Lewis 317 86 7th Most cited 25(1) Hogg & Terry 897 266

2001 Best Article 26(4) Mitchell & James 147 88 13th Most cited 26(1) Priem & Butler 992 264

2002 Best Article 27(1) Adler & Kwon 1916 450 1st Most cited Same

2003 Best Article 28(2) Benner & Tushman 555 180 1st Most cited Same

2004 Best Article 29(1) Biggart & Delbridge 77 30 12th Most cited 29(4) Phillips, Lawrence, & Hardy 291 96

2005 Best Article 30(1) Ferraro, Pfeffer, & Sutton 300 100 2nd Most cited 30(1) Inkpen & Tsang 459 143

2006 Best Article 31(2) George, Chattopadhyay, Sitkin, & Barden 44 21 25th Most cited 31(2) Johns 244 116

2007 Best Article 32(1) Dane & Pratt 103 36 7th Most cited 32(1) Sirmon, Hitt, & Ireland 197 57

2008 Best Article 33(4) Birkinshaw, Hamel, & Mol 41 7 5th Most cited 33(2) Matten & Moon 93 25

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This statement emphasizes notions of advanc- ing knowledge and moving the field’s thinking forward, providing new connections among pre- vious concepts, and exploring the practical im- plications of these connections. Interestingly, some thirty-five years later, a review of writings on theoretical contribution in AMR paints a pic- ture fairly consistent with this initial vision. Our synthesis of the literature indicated two key di- mensions along which the notion of “value- added contribution” is typically defined, as cap- tured succinctly by Kilduff: “Theory papers succeed if they offer important [read useful] and original ideas” (2006: 252). Our assessment of the current state of the art for publishing theory, perhaps especially in AMR, indicates that the idea of contribution rests largely on the ability to provide original insight into a phenomenon by advancing knowledge in a way that is deemed to have utility or usefulness for some purpose.

Given the historical progression of our field, the prominence of these two criteria (originality and utility) is perhaps not that surprising. Orga- nization and management studies started out with a couple of distinctive attributes: reliance on anecdotal evidence from business practice (there was little “scientifically” codified knowl- edge) and eclecticism (we borrowed from every- body). Before we could establish ourselves as a distinctive, scientifically rigorous field, we had to deal with both of these “shortcomings.” First, beginning in the 1960s and as a result of two reports critical of business education at the time (Gordon & Howell, 1959; Pierson, 1959), business schools (including management departments) began to emphasize more rigorous, quantitative orientations in an attempt to gain legitimacy within the larger academic community. By as- similating traditional academic standards and norms of knowledge generation and dissemina- tion from the physical and social sciences, this transformation helped move our field away from the criticism that management and organization- al knowledge was mainly a collection of anec- dotes and case studies. Second, at about the time of the founding of AMR in 1976, manage- ment departments began to pride themselves on having become the academic repository of mul- tidisciplinary knowledge oriented toward man- agerial practice—management study became a focal point for the intersection of psychology, sociology, anthropology, economics, political

science, and so on. The product of this inter- section represented an attempt not only to as- semble insightful thinking to develop a more systematic approach to knowledge about man- agement (an attempt that some claim failed; see Pfeffer, 1993) but also to develop some distinc- tive domains of theorizing (e.g., decision mak- ing, leadership, institutional theory).

Since the 1970s, the field of organization and management studies has achieved some nota- ble and laudable accomplishments. We have, for instance, become much more conceptually and empirically rigorous (such that the nature of management theorizing is much stronger, in scholarly terms, than it was only a generation ago), which has helped allay concerns that our knowledge base is too anecdotal. We have also begun to develop an institutional field identity that is no longer based mainly on the notion of eclecticism; that is, the top management jour- nals are now seeing work that constitutes orig- inal organizational theorizing (not merely recy- cled and dressed up psychology or economics), which, in a recursive fashion, is now beginning to influence the very fields from which we once borrowed (Agarwal & Hoetker, 2007).

To better understand what the dimensions of originality and utility mean for those attempting to publish in the top management journals, it is necessary to explicate each notion in more depth. Interestingly, our synthesis of the litera- ture indicates that both dimensions further di- vide into two subcategories (see Figure 1). Orig- inality can be categorized as either (1) advancing understanding incrementally or (2)

FIGURE 1 Current Dimensions for Theoretical

Contribution

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advancing understanding in a way that pro- vides some form of revelation, whereas the util- ity dimension parses into (1) practically useful and (2) scientifically useful. Our following dis- cussion of these two main dimensions and their two subcategories is quite consistent with a common characteristic of many theoretical pa- pers—the ubiquitous 2 � 2 matrix.

Originality

Perhaps more than any other criterion, origi- nality stands out as the “dimension de rigueur” for AMR reviewers and editors. This is clearly seen in the first line of the current AMR mission statement—“The mission of the Academy of Management Review (AMR) is to publish new theoretical insights that advance our under- standing of management and organiza- tions”—as well as in editorial statements de- scribing preferences for submissions: “The mission of a theory-development journal is to challenge and extend existing knowledge” (Whetten, 1989: 491); “We judge the value-added contribution of each and every article based on the potential contribution of the articulated new insights” (Smith, 1997: 8); and “[All AMR papers should] improve our understanding of manage- ment and organizations, whether by offering a critical redirection of existing views or by offer- ing an entirely new point of view on phenom- ena” (Conlon, 2002: 489). Conlon’s distinction be- tween extending current understanding and offering “entirely new points of view” is similar to Huff’s (1999) distinction between contributing to a current conversation and starting a new conversation. Accordingly, it provides the basis for discussing originality as representing either an incremental or a more revelatory or surpris- ing advance in understanding—a subdivision that offers a more nuanced grasp of what re- viewers and editors currently consider to be a theoretical contribution worthy of publication.

Incremental insight. The notion that theoreti- cal contributions should progressively advance our understanding is a long-venerated one (Kaplan, 1964) and is well-represented in AMR’s (1976) initial statement of purpose (reread the original “Suggestions for Contributors” above). This orientation has been consistently and re- peatedly invoked over the years—for example, “The ultimate value-added test of an article is that it has moved scholars in a field or advanced

our theoretical understanding” (Smith, 1997: 7). In perhaps one of the most recognized articles on theory, Van de Ven reiterates Lewin’s (1951: 486) assertion that “nothing is quite so practical as a good theory” in this way: “Good theory is practical precisely because it advances knowl- edge in a scientific discipline, guides research toward crucial questions, and enlightens the profession of management” (1989: 486). Based on the (then) groundbreaking work of Dubin (1978), this perspective is rooted in the belief that what makes one theory preferred over another is ad- vancement toward “what is believed to be true” (1978: 13) or a state where “a group of people sharing an interest in some set of observations come to agree that one theoretical model best provides understanding or permits accurate pre- dictions about the observational set” (1978: 13). In practice, this is often reflected in the idea that “theoretical insights come from demonstrating how the addition of a new variable significantly alters our understanding of the phenomena by reorganizing our causal maps” (Whetten, 1989: 493).

The key to connecting this notion of advanc- ing understanding with the editor’s/reviewers’ crucial task of determining value-added contri- bution arises in how one defines “significantly” in the above statement— how much additional understanding must be provided to meet the significance criterion? Obviously, this is not an easy question to answer, which may help ex- plain why the incremental perspective on in- sight seems to have fallen out of favor with reviewers and editors of many top journals over the past ten to fifteen years. In fact, reading more recent editorial statements on theory de- velopment from a spectrum of management journals conveys the sense that the advancing incremental understanding perspective has be- come rather too closely associated with the no- tion of minor, marginal, or even trivial improve- ments, where small advances in our thinking about a phenomenon provide the means to progress through “normal science” (Kuhn, 1962). Although incremental improvement is arguably a necessary aspect of organizational research, especially in service to the contextualization of theory (cf. Johns, 2001; Rousseau & Fried, 2001; Tsui, 2006), current thinking at AMR and other top theory and research outlets seems to have shifted to a focus on theoretical contributions

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deemed to be more revelatory and nonobvious to organizational scholars.

Revelatory insight. An alternative to the diffi- cult-to-answer question “How significant an ad- vance in knowledge is needed to constitute a contribution?” rests in the idea that contribution arises when theory reveals what we otherwise had not seen, known, or conceived. In other words, new theory “allows us to see profoundly, imaginatively, unconventionally into phenom- ena we thought we understood. . . . theory is of no use unless it initially surprises—that is, changes perceptions” (Mintzberg, 2005: 361). Of- ten cited in advocacy for this perspective is Davis’s (1971) “That’s Interesting!” article, in which he argues that research that is novel or counterintuitive or that questions assumptions underlying the prevailing theory (as well as those of the reader) will generally be seen as more interesting and, thus, more likely to make an impact on the reader (and hence make an impact on the field through increased citations): “The best way to make a name for oneself in an intellectual discipline is to be interesting— denying the assumed, while affirming the unan- ticipated” (1971: 343). The key distinction here from the advancing understanding incremen- tally perspective (rooted in Dubin’s views on truth) is that “a theorist is considered great, not because his/her theories are [necessarily] true, but because they are interesting” (Davis, 1971: 309).

Beginning in the 1990s and rapidly ascending to prominence since, this idea that “all contribu- tions to AMR should be ‘novel, insightful, and carefully crafted’” (Brief, 2003: 7) has become a staple for editorial descriptions of desired AMR papers—“The challenge then for authors pub- lished in AMR will be to convince AMR readers ‘to see nature in a different way,’ even to violate paradigm-induced expectations” (Smith, 1997: 8; see also Gioia & Pitre, 1990, and Morgan & Smir- cich, 1980)—and is even boldly proclaimed on the current AMR website (“AMR publishes novel, insightful and carefully crafted conceptual arti- cles that challenge conventional wisdom con- cerning all aspects of organizations and their role in society”). This refocusing on surprise has transcended AMR and is now touted as the basis for contribution at the other top organization and management journals, including AMJ, as seen in Rynes’ articulation of reasons for paper rejection: “Reviewers are judging the results not

against prior literature, but rather against com- mon sense or the likely reactions of the ‘person in the street.’ . . . ‘Is this really surprising?’” (2002: 312) and Bergh’s likening of theory contri- bution to the rareness criterion of competitive advantage: “[Is] a contribution . . . surprising and unexpected? Is the contribution more of a common sense derivation, or does it represent a novel and unique insight? Originality is a criti- cal concern” (2003: 136).

Our synthesis of the existing literature thus points to insight based in original, especially revelatory, surprising, or even transformative thinking as a key factor affecting the attribution of a theoretical contribution at many of the em- inent journals in organization study, and per- haps particularly at AMR. Therefore, our point in highlighting this shift is not that incremental advancements cannot provide a theoretical con- tribution, but simply that many editorial teams and reviewers at our top journals now prefer insights that reveal a new way of understanding as the basis for determining theoretical contri- butions, and thus as a preference for assessing publication potential. Importantly, however, the capacity for revelation is not the only criterion; also widely accepted is the sense that to be deemed a contribution, theory must be useful or somehow have utility in its application, either for other organizational researchers or for prac- ticing managers.

Utility

Although most contemporary editors see reve- latory insight that discloses a new way of see- ing as necessary for a value-added contribution, it is rarely sufficient; the insight must be seen as useful as well. That is, it must have the potential to either “improve the current research practice of informed scholars” (Whetten, 1990: 581) or improve the current managerial practice of or- ganizational practitioners. Or, as Van de Ven argues:

A central mission of scholars and educators in professional schools of management . . . is to con- duct research that contributes knowledge to a scientific discipline, on the one hand, and to ap- ply that knowledge to the practice of manage- ment as a profession, on the other (1989: 486).

In general, scientific utility is perceived as an advance that improves conceptual rigor or the

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specificity of an idea and/or enhances its poten- tial to be operationalized and tested:

Theory can advance science by providing cohe- sion, efficiency, and structure to our research questions and design (Kerlinger, 1973; Van de Ven, 1989). In a very practical sense, good theory helps identify what factors should be studied and how and why they are related. A high quality theory also states the conditions and boundaries of relationships (Hitt & Smith, 2005: 2).

Alternatively, practical utility is seen as aris- ing when theory can be directly applied to the problems practicing managers and other orga- nizational practitioners face, or as Hambrick suggests, through “the observation of real-life phenomena, not from ‘scholars struggling to find holes in the literature’” (2005: 124). Hambrick’s larger point, however, is that such a practical problem focus is a good way to develop theory per se. Thus, theory directed at practical impor- tance would focus on prescriptions for structur- ing and organizing around a phenomenon and less on how science can further delineate or understand the phenomenon.

This bifurcated view on the usefulness of the- ory arises directly from the trajectory of our field’s history; traditionally pushed to produce insight for both the professional and academic realms, management scholars experience pres- sures to enact the norms of a bona fide scientific discipline (again, originating from the 1959 Pier- son and Gordon and Howell reports) while also—at least ostensibly—speaking to and helping improve the organizations we study. We say “ostensibly” because our review of the liter- ature reveals a very strong bias toward scien- tific usefulness as the driving factor in editorial thinking about theoretical contribution. Interest- ingly, however, these two “discrete” categories of utility are not necessarily mutually exclusive; there are examples of theoretical advancements that have the requisite capacity to improve both the practice of research and the practice of man- agement, with a necessary “translation” from the scientific to the professional (as evident in the original mission of the journal Academy of Management Executive—“to provide a bridge or a link among theory, research and practice”— and the research-oriented subsections of vari- ous practitioner-oriented journals). Yet the real- ity is that, excepting some passionate calls for change during Academy of Management presi- dential addresses (e.g., Hambrick, 1994; Huff,

2000), practical utility’s role in theoretical contri- bution seems to receive mainly lip service (e.g., several paragraphs on “practical implications” in the discussion section; see Bartunek & Rynes, 2010, for insight into the utility of these sections), especially in recent times. Most of the editorial statements advocating the practical utility of organization and management theories occur earlier in our field’s history, with more recent editorial statements virtually ignoring this as- pect of the utility dimension.

Implications of the Originality and Utility Dimensions

The upshot of our synthesis of the literature, then, is the recognition that the current state of the art for developing conceptual papers that are deemed to provide a theoretical contribution rests in a scholar’s ability to produce thinking that is original (and especially revelatory or sur- prising) in its insight and useful (preferably in a scientific manner) in its application. In our view, the originality and utility dimensions usually are treated as working together to produce vary- ing levels of theoretical contribution. Modeling their interaction in a 2 � 2 matrix (Figure 1) produces a basic insight about which papers ultimately succeed at the top management jour- nals (and, by implication, at AMR). Papers that display both original, revelatory insight and sci- entific usefulness (Quadrant 1) clearly stand out as most likely to pass muster with editors and reviewers (assuming they also satisfy other de- sirable criteria1). Papers that only fit one of the dimensions well—scientifically useful but with- out adequate originality (Quadrant 2) or revela- tory insight without adequate scientific useful- ness (Quadrant 4)—present a challenge to both author and editor and usually must undergo sig- nificant revision, at minimum, if they are to be seen as making a significant theoretical contri- bution and, thus, become acceptable for publi- cation. Finally, papers that score low on both dimensions (Quadrant 3) are likely to be desk- rejected or receive a firm rejection decision after the first round of reviews (and occasionally

1 As Whetten outlines, “Is the paper well written? Does it flow logically? Are the central ideas easily accessed? Is it enjoyable to read? Is the paper long enough to cover the subject but short enough to be interesting?” (1989: 495).

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what one of the authors calls an “RWS”—a “Re- jection With Scorn”).

Ultimately, our synthesis of the theoretical contribution literature and its representation in our simple 2 � 2 model lead to several observa- tions about the current practice of making a contribution to theory. First, the dimension of original insight with the power to reveal a new way of seeing is likely to remain a perennial norm at all elite, theory-driven management journals, including AMR. We feel confident in making this less-than-bold prediction because, by its very nature, theorizing depends on new concepts to maintain idea vitality in the field. Incremental advances in theory simply cannot produce this energy and, although necessary in their own right, are unlikely ever to become the foundation on which a high-impact theory- building journal rests. Second, utility in the form of scientific usefulness also is likely to remain an important aspect of the norms for theoretical contribution for the foreseeable future, simply because scientifically useful ideas are critical to the larger project of establishing theory that is conceptually rigorous and internally consistent and, thus, the surest path to building and main- taining academic legitimacy. Additionally, sci- entifically useful ideas do a better job of contrib- uting to the theoretical developments of other scholars who are also working to further legiti- mize the scholarly field of organization and management studies.

That said, after our attempt to synthesize the existing literature about attributes that consti- tute a contribution to theory, we were uneasy with simply accepting what the (mostly edito- rial) literature portrayed as a theoretical contri- bution. Part of this unease arose from our read- ing of both the AMR Best Articles and most cited papers listed in Table 1, which revealed that although the majority of these papers could be classified as being original in their ideas, those that provided revelatory insights did so not so much by introducing new concepts (as the typi- cal editorial depiction would have it) but much more often by offering a novel approach to inte- grating prior thought and research into some model or framework that constituted a different way of understanding some phenomenon.2 More

important, we also began to notice a subtle theme distinguishing the most cited papers from the Best Articles: although both sets of papers could be considered high in scientific utility, the most cited papers could more often also be char- acterized as higher in utility for practice. If arti- cles receiving the most citations do a better job of bridging scientific and practical usefulness, this suggests the possibility of a unifying di- mension that can account theoretically for both scientific and pragmatic value (i.e., a notion we would label scope). This also suggests the pos- sibility of expanding our conceptualization of what constitutes a theoretical contribution if we can identify ways of enhancing our ability to achieve more scope in our theorizing.

CONTRIBUTING TO THEORY ABOUT MAKING A THEORETICAL CONTRIBUTION

Adhering to the same standards for consider- ation we just reviewed, we believe there is room for a contribution in the process of building some new theory about the work of theory build- ing itself—an unaddressed opportunity for our field to take the next step forward in maturity by extending our conceptions of what makes for a theoretical contribution. There are two consider- ations that suggest a strong need to move from where we are now to a more advanced plane of thought and wider influence. First, Katz and Kahn (1966) observed that organizations and in- stitutions can (and often do) have multiple, dis- parate roles in society. Academia as an institu- tion—and perhaps especially in the form of a professional academic institution like a school of management— has a dual and somewhat par- adoxical role: we are the “keepers of the flame” in disseminating tried-and-true ideas and prac- tices (usually via teaching but also via consult- ing), which Katz and Kahn term a maintenance role—a role that has the effect of structuring, stabilizing, and institutionalizing knowledge

2 In fact, we initially used the categories “incremental” and “transformative” to characterize the originality dimen-

sion because we were trying to summarize and synthesize the content of prior writings by scholars discussing “What is a contribution?” Instead, after reading the Best Articles and most cited AMR papers, what we actually saw in practice was a dimension that is better categorized as incremental or revelatory, because relatively few of even these stellar pa- pers could be labeled as transformative in the literal sense. On balance, most of these AMR articles are original in the way they integrate, rather than in the way they create, new concepts.

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and action; simultaneously, however, manage- ment schools are also charged with being in the vanguard in generating new knowledge (via cutting-edge theory and research) that serves to question received wisdom and accepted prac- tice and, thus, to undermine “the way we do things around here.” Katz and Kahn (1966) term this an adaptive role in society, and it serves as a substrate for transforming the social order. From our perspective, we are currently devoting much more energy to our maintenance role (via teaching,3 if not practice-oriented research) and underplaying our putative adaptive role. Orga- nization and management science has, there- fore, come up short in fulfilling the charge of being on the leading edge of management thinking. Indeed, most of the new ideas in man- agement that have been put into practice have come from the world of practice, rather than from academia (cf. Barley, Meyer, & Gash, 1988). Consequently, society has granted us respect, but not much influence (see Mintzberg, 2004, and Pfeffer, 1993). We believe our field has matured to a point that the time has come to begin recti- fying that shortcoming.

As our retrospective on management and or- ganizational theorizing suggests, the dimension of utility has historically been defined accord- ing to two tracks—scientific usefulness and practical usefulness—with a relative neglect of the latter. This neglect is somewhat understand- able because practical utility is most often con- sidered as addressing specific problems with- out necessarily tapping general principles, whereas good theory emphasizes generalities (with appropriate boundary conditions identi- fied). On these grounds we clearly have as- signed more importance to scientific utility, which, although understandable, is perhaps something of a misconstrual for a scholarly field that is so intimately associated with a professional practice domain (and schools of management are arguably more akin to schools of law or medicine than those of eco- nomics or sociology).

Second, the fact that rigorous scholarship is not often deemed by outsiders to be relevant scholarship that both ministers to and antici-

pates societal needs suggests that we have not devoted appropriate attention to the expectation that good scholarship should not only have practical relevance but also some degree of fore- sight in identifying important coming issues and problems that need to be conceptualized. One source of the problem is that management scholars have, in effect, created a closed indus- try engaged in producing knowledge intended mainly for other academic knowledge produc- ers. This outcome is a consequence of overem- phasizing scientific importance (in part because scientific importance tends to generate special- ized language that only other cognoscenti can understand; see Bennis & O’Toole, 2005).

Simply put, we believe that theoretical contri- butions in management and organization stud- ies have not done an adequate job of anticipat- ing the important conceptual, as well as practical, needs of society’s now most prominent members— business and social organizations. As Staw outlined the problem for OB research some twenty-five years ago: “The field may not have even served managerial interests well, since research has taken a short-term problem focus rather than having formulated new forms of organization that do not currently exist” (1984: 629)—an orientation that implies that we as a field are also guilty of employing short-term thinking, which Norman Lear has called “the social disease of our time” (cited in Bennis, 2003: 15) and which undermines our ability to contrib- ute to organizational and societal adaptiveness. This is a nontrivial shortcoming in our ap- proaches to making theoretical contributions that could have a much wider impact—a short- coming we believe could be addressed by en- couraging an orientation toward prescience in trying to anticipate, conceptualize, and influ- ence significant future problem domains. We next consider these two related deficiencies in our theorizing as avenues for better fulfilling our adaptive role in society.

Relevance to Practice As a Prominent Dimension of Theoretical Contribution

As implied above, the maturation of our disci- pline has seemingly moved us farther away from the very spheres of society we originally set out to influence. Consider the following an- ecdotes, each of which in its own way is quite telling about the current character of our theo-

3 We acknowledge that many instructors work to include new knowledge into their courses, yet the practical fact is that the overwhelming content of most courses constitutes accepted theory and practice.

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retical enterprise. The first story goes that in the early 1980s one of the officers of the Academy of Management concluded that as one conse- quence of the shift toward conceptual and em- pirical rigor then sweeping the field, the rele- vance of our theories to managerial practice was waning. As a step toward redressing this trend, he decided that our field needed to “con- nect” better with practicing executives. To that end, he hosted a number of high-level managers at the next annual AOM meeting. He shep- herded the entourage around to various ses- sions, symposia, and social events, but they were not very forthcoming about their impres- sions of the proceedings. At the end of the day, the hosting professor, who could contain himself no longer, explicitly asked what they thought of the work of the academic management profes- sion as manifested by the events of the day. Uncomfortable silence. One of the executives thought it over for a few pregnant seconds, how- ever, and then said simply, “You people talk funny.”

A second anecdote involves one of the au- thors, who was discussing the criteria for Ph.D. student selection with his colleagues. There was little debate about the relevance of GMAT/GRE scores, grade point averages, experience with the research process, and so forth. Yet when he suggested that because it was a professional school organizational experience should be con- sidered as well, another professor responded that practitioners were “not our audience” and that work experience had not been shown to correlate with Ph.D. program success and, there- fore, should not be included on the list of desir- able criteria.

A final example hints at the difficulty of rec- onciling academic and practitioner assess- ments of theoretical contribution and value. In 1985 Cummings and Frost edited a volume enti- tled Publishing in the Organizational Sciences, a compendium of writings, opinions, and advice about what it took to succeed when trying to publish in management journals. Early in that volume an academic writer touted the marvel- ous contribution offered by Gronn’s (1983) article “Talk As Work.” Curiously, later in the same volume a practitioner writer independently de- rided the same work as trivial and obvious to any practicing manager.

The roots of our disconnect from practical util- ity. From a layperson or practitioner perspec-

tive, we academics do indeed “talk funny.” From our point of view, we do so for good reasons. Parsimonious theoretical language saves time and space and (we hope) enhances clarity for other scholars; theoretical notions tend to be specified in abstract terms that capture concep- tual meaning. Yet we should recognize that our specialized language tends to distance us from the issues that generated the theories about the phenomena we are trying to describe and ex- plain in the first place. Put differently, our distal language often seems to elide the relevance of our second-order theoretical constructs from the proximal parties whose experience we are try- ing to explicate.4

Worse, perhaps, the increasing distance be- tween our theories and their practice referents is sometimes justified on the grounds that theory and practice are “different worlds” and need not have a close relationship (as implied by the Ph.D. admissions debate). The difference of opinion about the worth of a given academic article highlights the common view that the sub- jects of our theorizing do not seem to attribute much significance or value to our theorizing—a nontrivial issue if we hope to enact an influen- tial stance toward our adaptive role in society. Shapiro, Kirkman, and Courtney (2007) argue that there are actually two sources for this “talk- ing past each other” dynamic between scholars and practitioners, which they term the lost be- fore translation problem (ideas that are essen- tially irrelevant to practice even before theo- ries are formulated or studies are conducted) and the lost in translation problem (difficulty in explaining the relevance of theories or find- ings to practice).

Relevance to practice is actually a long- standing theme in our writings about theory and theoretical contribution (Bergh, 2003; Hambrick, 1994; Thomas & Tymon, 1982), especially in terms of empirical research (see the rigor versus rele- vance debate in Gulati, 2007; Palmer, Dick, & Freiburger, 2009; Polzer, Gulati, Khurana, & Tushman, 2009; and Tushman & O’Reilly, 2007, for examples). Yet evidence that we have paid serious attention to this de facto platitude in our theoretical efforts is woefully lacking. Our rela-

4 Consider the last two sentences. To illustrate our point, we wrote the first in plain English and the second in academese.

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tive inattention to a bona fide concern with the practical applicability of our theories has led to a troubling disconnect between management theory and practice (Ghoshal, 2005; Mintzberg, 2005; Pfeffer, 1993)—an observation that gives rise to a consequential question: How might we accomplish a reconciliation of academic and practitioner standards for judging contribution?

First, it is important to reiterate that our theo- ries should be problem driven5—that is, in some fashion addressing a problem of direct, indirect, or long-linked relevance to practice, rather than narrowly addressing the (theoretical) “problem” of finding the next mediator or moderator vari- able or filling theoretical gaps simply because they exist. When we focus mainly on the latter, we end up advancing theory for theory’s sake, rather than theory for utility’s sake. Simply put, the focal problems in our chosen field of work (organization study) should relate more directly to the wider world’s work (organizational prac- tice) by drawing more from the world of practice and the experience of real people, rather than from abstract derivations of hypothetical formu- lations. This, ideally, would lead to an integra- tion of the scientific and practical utility dimen- sions and would produce a comprehensive utility dimension better aligned with the notion of scope.6 As an example, one of the AMR Best Articles that also was that year’s most cited pa- per (and, not coincidentally, the most cited pa- per on Google Scholar of all those in our AMR sample) provides a good exemplar of theorizing that has scope. Nahapiet and Ghoshal (1998) provided theorizing having both scientific and practical utility that deals with a topic of inter- est for a broad audience and integrates existing views into a coherent and comprehensive theo- retical model.

Second, and as already noted, we should em- brace the fact that we are a profession (aca- demia) studying another profession (manage- ment), so our orientation toward theoretical contribution should include an explicit appreci- ation for applicability. We want to be clear,

however, that we are not arguing that we should take our lead for new theorizing from practition- ers’ specifications of mundane managerial problems— unless, of course, they are manifes- tations of wider or deeper issues. We should instead be aspiring to address significant prob- lem domains that either require or will soon require theorizing. As Mintzberg (2005) points out, methodological (and even theoretical) rigor often interferes with both insight and relevance, perhaps especially when dealing with grand- level issues or problems. Bennis and O’Toole (2005) have accused us of delimiting the scope of our studies only to those variables we can easily measure, producing a kind of “methodolatry” that harbors the paradoxical possibility of blinding rather than illuminating things that re- ally matter. The fact that Bennis and O’Toole’s article appeared in Harvard Business Review, whose readership is heavily oriented toward re- flective practitioners and who on reading the article would further dismiss the relevance of the academic study of organizations, only deep- ens the hole out of which we must climb.

Practical versus practice-oriented theoretical contribution. In our view, one of the inhibitors of the relevance of our theorizing is that we have been treating the notion of pragmatic utility as practical utility. Based on conversations with colleagues who are reticent to formulate practi- cal theory or conduct practical research, we sus- pect that there simply is not enough profes- sional “gravitas” associated with theory that might have obvious practical application. Such ideas are not seen as “big enough” for grand- level theorizing. A small shift in orientation might make a big difference in the contribution of our theories to addressing important prob- lems, however. Focusing on the weightier notion of practice (with its pedigree in the deep philo- sophical traditions of American pragmatism) would not only signal to scholars that we are working on significant issues but would provide a firm intellectual basis for theoretical formula- tions with pragmatic relevance.

The scholarly roots of a practice approach can be traced to James (1907, 1909) and Dewey (1938; Dewey & Bentley, 1949), who viewed theoretical knowledge not as an “object” to be possessed but as a dynamic phenomenon that manifests in the act of knowing something. The move from objectified, static knowledge to dynamic pro- cesses of knowing shifts the focus of theorizing

5 Ideally, theories should also be opportunity driven—that is, anticipating opportunities for enlightened practice, in a fashion perhaps best exemplified by the positive organiza- tion studies (POS) movement (e.g., Cameron, Dutton, & Quinn, 2003).

6 Thanks to both Don Hambrick and one of our reviewers for discussions relevant to the notion of scope.

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to the activities that people engage in while dealing with problems. In this view the act of knowing influences what is known and how it is known (see also Morgan, 1983, and his discus- sion of “research as engagement”). Knowledge, therefore, inheres in the activities that individ- uals engage in to deal with their day-to-day interactions. This pragmatist philosophical ori- entation has had some influence on organiza- tional scholarship. Pentland (1992), Cook and Brown (1999), Brown and Duguid (2001), Or- likowski (2002), and Nag, Corley, and Gioia (2007), among others, all have studied connec- tions between the content knowledge of organi- zation members (i.e., what they know) and their social practices (i.e., what they do). Cook and Brown (1999) treat practices as actions informed by meanings grounded in specific contexts. In this fashion, knowledge is viewed more as a recursive dialogue between practice (action) and meanings (cognition).

It is only a small leap from these works, which focus on people at work, to treating ourselves (as theorists) in a similar fashion as we examine our theorizing practices and our assumptions about what constitutes a contribution. In this light it becomes apparent that we should con- duct a more intimate dialogue between practice (actions of practitioners) and meanings (theoret- ical contributions that both derive from and in- form practice). A practice view of theoretical knowledge also connotes a significant shift be- cause focusing on theoretical knowledge as somehow independent of its pragmatics over- looks the processes through which knowledge use, value, and utility emerge “from the ongoing and situated actions of organizational members as they engage the world” (Orlikowski, 2002: 249).

The most important insight from a practice orientation concerning the assessment of theo- retical contribution is that theoretical knowl- edge does not exist as a set of theory-building rules independent of actual practice; rather, it becomes inextricably intertwined with the man- ifestations of the theoretical knowledge in prac- tice (and vice versa). The two key notions arising from adopting a practice view of knowledge, then, are (1) that knowledge should be treated as process and (2) that the production of knowledge should be treated as a recursive dialogue be- tween theorists and reflective practitioners. The upshot of this orientation is that merely holding

theoretical knowledge contributes little if that knowledge is not exhibited in organizational practice and does not affect practices other than our own theorizing practices. In addition, how- ever, widely influential theorizing should also hold the potential for trying to identify domains that will soon be in need of theorizing (e.g., vir- tual societies, sustainability, accelerating glob- alization, new models of management not based on the preeminence of economic factors).

An Orientation Toward Prescience to Increase the Utility of Our Theoretical Contributions

On what level might scholars most influence practice? As noted, because our theoretical work is aimed at more general formulations, it is often removed from direct application to particular problems. For that reason our potential for influ- ence in practical domains is often limited. If we want to have more influence on society’s conver- sations and better fulfill our adaptive role in society, we also should direct our energies and capabilities at focusing on the future of manag- ing and organizing. Such an observation sug- gests that we should try to theorize about incip- ient organizational, managerial, and societal issues and problems—that is, we should work to develop what we term theoretical prescience. Prescience is most often defined in terms of fore- knowledge, foresight, or forecasting of events. For the purposes of better executing our adap- tive role, however, prescience involves antici- pating and influencing the type of managerial knowledge needed to deal with coming societal and organizational concerns. More specifically, theoretical prescience can be defined as the pro- cess of discerning what we need to know and influencing the intellectual framing of what we need to know to enlighten both academic and reflective practitioner domains. In our view, pre- scient scholarship not only fulfills the usual role of supplying conceptual knowledge used almost exclusively in scholar-to-scholar communiqués but also anticipates the conversations both scholars and societal leaders should be having and influences the framing of those conversa- tions in conceptual terms.

On theoretical prescience. Abraham Lincoln is often credited with the observation that “the best way to predict the future is to create it.” Computer scientist Alan Kay famously articu- lated a small adaptation of this pithy statement

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in posing that “the best way to predict the future is to invent it.” We would suggest a modest variation on this theme by noting that perhaps the best way to predict the future is to influence the conversation about what it could or should be. This orientation includes but goes beyond the notion of detecting “weak signals” (Shoe- maker & Day, 2009) and discerning where trends are likely to lead— or, as Bennis has put it, “It’s not as important to know where the puck is now as to know where it will be” (2003: 194; citing hockey star Wayne Gretzky). Prescience, in our view, involves not only sensitivity toward devel- oping trends but acting to influence those trends via prospective sensemaking (Gioia, Corley, & Fabbri, 2002; Weick, 1979, 1995) and sensegiving (Gioia & Chittipeddi, 1991; Maitlis & Lawrence, 2007)—in other words, giving meaning to ambig- uous informational cues and articulating viable interpretations and actions to cope with coming organizational and environmental demands.

In terms of broadening the scope of our theo- retical contributions, then, we do not view pre- science as a matter of “predicting the future” or gazing at a crystal ball. Prescience in our terms is a matter of anticipating and, more important, influencing the definition of significant organi- zational problem domains to illuminate an im- portant area for consideration—that is, drawing attention to areas we need to understand from a theoretical point of view that have relevance for significant organizational and societal issues and problems—as opposed to trying to predict the next big theory from a purely intellectual viewpoint and, thus, increasing the likelihood of creating the next managerial fad (see Abraha- mson, 1991). An orientation toward prescience accentuates the notion that we in academia should be leading-edge thinkers—we should be- come more oriented toward advancing not only the field’s relevance to future scholarship but also the field’s relevance to reflective practice concerning problems that matter (Pfeffer, 1993; Schön, 1983).

For instance, it is apparent that sustainability is an important issue to theorize about for the foreseeable future. Sustainability is currently viewed as “atheoretical,” so it becomes appar- ent that prescient theoretical work should be devoted to issues of sustainability and other concepts in its nomological net (e.g., implica- tions of global climate change for organizing and organization [Gjelten, 2009] and employee

and leadership issues arising from the eco- nomic shifts accompanying green organizing and green firms). Or consider the emergence of do-it-yourself (DIY) manufacturing (Anderson, 2010), a rising phenomenon involving virtual teams that develop open source plans for ob- jects such as circuit boards, custom tools, furni- ture, and even cars, which are then outsourced to a small batch manufacturer who produces a prototype and offers to set up production for a set price (if it is not intended to be a one-off project). These small, extremely flexible, and surprisingly profitable companies represent a new form of organizing better suited for dealing with an era where transaction costs become al- most nonexistent because of the potential for distributed innovation in our digitally intercon- nected society (Lakhani & Panetta, 2007).

Other current examples of nonobvious orga- nizing (e.g., Linux, Wikipedia, Grameen Bank) suggest that our theorizing has done an inade- quate job of anticipating and accounting for these kinds of organizations, a problem likely to be magnified in the future if we do not encour- age some form of prescience in our theorizing. The implications for organizational theories, from the micro (e.g., psychological contracts, compensation/motivation, leadership) to the macro (e.g., organizing, institutional change) and strategic (competitive dynamics, agency theory), could be significant. Similarly, one could imagine prescient management theory touching on issues ranging from demographic shifts in society (affecting our OB and HR do- mains) to social changes arising from techno- logical advances (e.g., value of privacy, virtual societies, artificial intelligence) to strategic/ institutional changes arising from trends in lo- cal and national governance.

Because the current view of what constitutes a contribution is oriented toward making judg- ments mainly on the basis of conceptual origi- nality and utility—where utility is rather nar- rowly defined as useful for further (scientific) concept development—we believe our scholarly community needs to try to develop an orienta- tion toward prescience to make informed infer- ences about what will be important to know and to conceptualize. To broaden the scope of our influence in making theoretical contributions, management scholars need to more credibly en- act our adaptive role by generating theory that anticipates problem domains that will inform

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future thought and action.7 Incorporating a fu- ture orientation can help keep our theories not only vibrant but also relevant in a constantly changing landscape of organizational realities. Additionally, we believe that over time, as pre- science becomes more prominent in our theoret- ical formulations, the distinctions between sci- entifically useful and practically useful will begin to blur.

Attributes of prescient scholarship. Although we recognize that not all organization- al/managerial scholars will (or should) try to adopt or practice prescient theorizing, we none- theless think it is important for the field to en- courage those interested in attempting to build prescient theory. Toward this end, we identify two key attributes that would be hallmarks of prescient scholarship.

First and foremost, prescient theorizing would direct attention toward future problem domains. Prescient scholars would first attend to cues in the present in a way that suggests that some consequential issues or problems might need to be addressed by management scholars in the future. This orientation does not involve some sort of academic clairvoyance but, rather, a fo- cus on what we might term projective futurism. As an example of such an orientation, climatol- ogy data indicate that global temperatures are within historical fluctuations, so we cannot ob- jectively assert that the globe is warming. Yet because of rising levels of various greenhouse gases and so forth we have sound theoretical bases for arguing and predicting that climate change is a threat and will soon be demonstra- bly out of the envelope of normal fluctuations and, therefore, that prudent action is necessary now. Those actions are likely to have implica- tions for organizing differently, and we should try to be anticipating possible theoretical impli- cations. The same could be said for advances in artificial intelligence and the impact they will have on workforce decisions and strategic plan- ning in organizations of the future, or changes in privacy law following in the wake of popular social networking technologies. Likewise, pay-

ing attention to popular press and news sources that report on cutting-edge business can provide early insight into new phenomena (like the DIY manufacturing example) that serve as a harbin- ger of emerging trends. Similar logic applies to our existing theories of organizing and manag- ing; a prescient theorist would ask, “What is it about current models that are insufficient to ac- count for likely future trends such that we need different or embellished theories to account for reasonable projections?”

Prescient scholars would, therefore, develop an orientation toward prospection—they would assume the role of making informed projections about coming issues, act as if those issues have manifested, and then infer what theoretical do- mains need attention or invention. The military, for instance, has noted that traditional orienta- tions and actions have involved informed retro- spection, which has enabled it to better fight the last war. The military’s new orientation is to ask, “In what ways can we prospectively imagine how to better fight the next war?” The tradi- tional retrospective sensemaking orientation (wherein we ask ourselves what consequences our actions have had, leading to a better under- standing of the past) inevitably produces refine- ments in current ways of thinking. Organization studies have been mostly retrospectively ori- ented, which has had the consequence of fulfill- ing mainly our “maintenance” role in society. We would benefit from adopting a notion of pro- spective sensemaking (Gioia et al., 2002), even if it is usually a variation on the theme of retro- spective sensemaking (Weick, 1979)—that is, casting ourselves figuratively into the future and acting as if events have already occurred and then making “retrospective” sense of those imagined events.

Second, and equally important, prescient the- orizing involves a focus on sensegiving. It is not enough simply to refine our prospective sense- making abilities. It is also important to articu- late the sense made in a way that affects the character of both academic and reflective prac- titioner discussions, as well as the spectrum of possible actions that ensue from exercising in- fluence over the framing and tenor of the discus- sions—that is, we need to become more adept at sensegiving (i.e., Gioia & Chittipeddi, 1991; Maitlis & Lawrence, 2007). It is in this domain that we can better fulfill our adaptive role in society. Doing so implies more attention not only

7 We are not advocating that all or even most theoretical efforts should aim for prescience, or that prescience should become a key dimension for manuscript evaluation. We are suggesting, however, that an orientation toward prescience should become a not uncommon hallmark associated with some of our best theorizing.

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to new ideas but ideas that have a more proxi- mal relationship to practice than has been our tradition. This means finding ways to communi- cate our sense made (i.e., our theoretical contri- butions) such that those most likely to find our work pragmatically useful (i.e., thoughtful prac- titioners) understand it and are motivated to ap- ply it.

Consider an endeavor that is parallel to the task of trying to gauge contribution—trying to assess “creativity.” Creativity in business is dif- ferent from creativity in the arts. Creativity in the arts is usually defined mainly in terms of novelty (Amabile, 1996). In business, however, creativity has two key dimensions: novelty and pragmatic value (Ford & Gioia, 1995). We would argue that we should be encouraging both of these dimensions in trying to formulate contri- butions to theory that have wider scope; in other words, we should be offering not just original or revelatory insights but new insights that are valuable for advancing ideas with a praxis di- mension—melding two of Aristotle’s three kinds of knowledge, theoria (theory) and praxis (prac- tice)—in a way that practice informs theory, and vice versa. As we have noted above, historical writings in organization studies have acknowl- edged these orthogonal dimensions implicitly (i.e., in the form of the originality and utility criteria), but the de facto outcome has been no- tably more attention to the originality criterion. We believe an orientation toward prescience would enhance our potential for grander scope in making theoretical contributions.

DISCUSSION

Precisely what constitutes a theoretical con- tribution in organization and management stud- ies is a vexing question that cannot be an- swered definitively, although it does seem to have a conventional answer—for example, “The notion of contribution—like many other abstract concepts, such as quality or truth—is somewhat subjective and can only be assessed in the con- text of each unique manuscript” (Rynes, 2002: 311). Our initial approach to addressing this question was to review the existing literature and provide a synthesis of current views. That synthesis suggests that theoretical contribution presently has two germane dimensions, origi- nality (classified as either incremental or reve- latory) and utility (scientific and/or pragmatic

usefulness), with a strong preference in the scholarly community for works that are revela- tory/surprising and carry mainly scientific value. We have summarized the current idiom for declaring a theoretical contribution in Figure 1, which provides a framework for scholars to assess whether an idea will be seen as making a theoretical contribution.

If we take a more critical and expansive view of our scholarly potential and ask whether it is possible to make the grand notion of “theory” more pertinent to solving significant manage- rial and societal problems, we might ask the more pointed question, “What would constitute a theoretical contribution beyond that engen- dered by the currently accepted criteria—that is, a contribution to theory that is relevant not only for scholar-to-scholar consumption but one with greater scope and potential to influence current and future organizational practice?” We agree with Whetten’s assertion that “the mission of a theory-development journal is to challenge and extend existing knowledge” (1989: 491). Yet we would encourage a conceptualization of an even more robust theory, one that has greater reach and would enable organization studies to real- ize its potential as both thought leader and prac- tice leader in the wider society. We take seri- ously Katz and Kahn’s (1966) observation that organizations and institutions can be viewed as fulfilling various societal roles, and we hold to the ideal that academia is charged with the responsibility of fulfilling both maintenance and adaptive roles in society. Our assessment of the current criteria for judging theoretical con- tribution, however, has led us to conclude that we have not enacted our adaptive role as well as we could. For that reason our approach to making a contribution to theory in a paper about theoretical contribution is to suggest a renewed and recursive consideration of the practice ele- ment for theory development, in part by suggest- ing that authors adopt an orientation toward prescience as an avenue not only to improve our relevance to practice but also to enhance our influence in society.

Huff (1999) memorably characterized research and writing as a series of multidimensional con- versations. To get the most out of each of these conversations, she counseled that we scholars consider four guiding questions. Our concern with importance for practice, foresight, and sensegiving has implications for each of these

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questions: (1) “Which conversations should I participate in?” (those that will make the great- est difference for science and practice); (2) “Who are the important ‘conversants’?” (scholars and practitioners); (3) “What are scholars talking about now?” (answer this question mainly for the purpose of discerning a point of departure for tomorrow’s question); and (4) “What are the most interesting things I can add to the conver- sation?” (those that direct conversation toward what needs to be known for the present and the future).

If we attend to the overarching message con- veyed by the relevance of practice and pre- science to our theorizing, it encourages us as theorists to raise our own awareness of the lim- itations of our historical ways of thinking and suggests viable grounds for reconsidering how we might think more broadly about our most important activity— generating new theory with scope (i.e., theory that contains both scientific and pragmatic usefulness). Thinking in such terms also encourages us to be a bit more intel- lectually adventurous. As Mintzberg has noted, “If there is no generalizing beyond the data, no theory. No theory, no insight. And if no insight, why do research?” (2005: 361). We would add that if theory does not have the potential for foresight and for changing the conversation, why do the- ory building? Our charge, then, is to become more expansive in our theorizing, to work to infuse our theorizing with significance for prac- tice—present and future—and to “give sense” to wider communities within society about the rel- evance of our theoretical work.

On Practice

If we embrace the idea that we are scholars charged with the responsibility of generating and disseminating useful knowledge, then the notion of utility simply must extend beyond the implicitly accepted idea that “useful for theory development” is the sole criterion of conse- quence and begin to account for relevance to practice in a much more substantive manner. Kilduff notes that “the route to good theory leads not through gaps in the literature but through an engagement with problems in the world” (2006: 252). This sort of observation means that we must begin to “choose our theories according to how useful they are, not how true they are” (Mintzberg, 2005: 356). Our current tradition has

tended to turn us into a closed community con- ducting a dialogue with ourselves (Miller, Greenwood, & Prakash, 2009), which implies that we have unwittingly focused some of the best minds in the world on a sphere too small for their capacity for greater contribution. We can- not be a closed community if our intent is to influence current and future organization stud- ies and practice (which should be our intent, given our adaptive role in society).

We are a professional field (Adler, 2006; Pfef- fer & Fong, 2002). Rather than downplaying the importance of pragmatic contribution, we should celebrate it by formally bringing that dimension more prominently into our judgment structures and processes. We need to focus more on contributions of a grander scope by including utility for practice in our assessments of theory. To date, our most influential (and most highly cited) theories (e.g., macrolevel theories, such as new institutional theory, resource dependence theory, contingency theory, agency theory, and transaction cost theory; meso theories, such as social capital and organizational identity and organizational learning; and microlevel theo- ries, such as equity theory, procedural justice theory, goal theory, and prospect theory) have been formulated for scholars but nonetheless have major pragmatic implications that expand their scope (see Adler & Kwon, 2002; Benner & Tushman, 2003; Nahapiet & Ghoshal, 1998; Ol- iver, 1991; Reed & DeFillippi, 1990; and Ring & Van de Ven, 1994, for AMR articles we believe exemplify this notion of scope). How do we get such scope? By thinking in a more encompass- ing fashion about what we ought to be doing as theorists. One avenue for doing so is to pursue a practice view of knowledge generation (i.e., the- ory development) in the venerable philosophical tradition of American pragmatism.

Our arguments in this paper resonate with those in a recent spate of articles focused on the issue of balancing methodological rigor and practical relevance in empirical management research (see the “Editor’s Forum” in volume 50, issue 4, of the Academy of Management Journal and the “Editor’s Choice” section in volume 18, issue 4, of the Journal of Management Inquiry). All address the general question of how busi- ness schools can better “pursue fundamental understanding of phenomena with the goal of tackling major real-world problems” (Tushman & O’Reilly, 2007: 769). Unfortunately, an implicit

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assumption in much of this debate appears to be that scholarly journals that favor theoretical de- velopment eschew pragmatic relevance—a be- lief seemingly based in the peculiar assumption that theoretical contribution and pragmatic rel- evance are somehow incompatible (see Tush- man & O’Reilly, 2007, for an exception). They are not; theoretical contribution and pragmatic rel- evance clearly can and sometimes do work hand in hand. There is nothing about the nature of either theory or practice that prevents them from being served simultaneously (cf. Gulati, 2007). Ultimately, we believe the dimensions of originality and utility/scope can come together to produce theories that make a difference for science and practice. The question is simply whether we as an academic discipline can change our own practices to better account for the issues and problems central to the organi- zations we study. We believe that achieving scope in our theorizing should be an institu- tional goal for our field.

On Prescience

Those from outside academia reading our the- oretical work might reasonably conclude that we have a rather impoverished view of what constitutes a contribution if we emphasize mainly clever insights and intellectual useful- ness. As Polzer et al. note, “The failure of busi- ness school research to either anticipate or deeply understand some of the most fundamen- tal challenges of our times threatens the legiti- macy of our enterprise” (2009: 280). In a turbulent era of organizational ambiguity and complexity, a key task is to try to be prescient about what is important to theorize about—and such pre- science will undoubtedly lead us to focus on problem domains with significant import for fu- ture practice. Relatedly, Kilduff, citing Lakatos (1970), notes that one of the “important criteria for evaluating theory is the extent to which it runs ahead of existing empirical research in terms of alerting us to research opportunities hitherto unanticipated” (2006: 252–253). To this observation we would add that our theorizing should not just be running ahead of empirical research but, rather, should be anticipating coming conceptual domains in need of theory and research.

Hambrick, in his critique of our field’s overem- phasis on theory, agrees with Helfat (2007) in

proposing that we begin by generating practical facts “that can inform us as to what we need a theory for” (2007: 1349). Of course, we theorists are not necessarily attuned to the complex dy- namics of the organizational world, and we could use some help in picking up the weak signals (Shoemaker & Day, 2009) that suggest areas ripe for theoretical development. Penn State’s Smeal College of Business publishes a periodic “Early Indications” electronic newslet- ter written by a practitioner-academic who keeps his antennae tuned to the business envi- ronment. Similarly, the School of Information Science and Technology’s “Institute for Global Prescience” is run by a “Professor of Practice” (similar to the thirty-person foresight staff at Mercedes-Benz’s Society and Technology Re- search Group). There also are organizations that are attuned to future trends, such as the Institute for the Future (iftf.org), the McKinsey Global In- stitute (mckinsey.com/mgi), and Deloitte’s Cen- ter for the Edge (Deloitte, 2009). Each of these early-warning systems signals issue and prob- lem domains in need of conceptual development and raises the possibility that even the way we structure ourselves to generate and disseminate theory may need to change.

Our view of prescience, however, encourages scholars to become not only early sensemakers but also early sensegivers—that is, not only to see the coming wave but to attempt to shape the conceptual conversation by influencing the pre- mises on which the conversation is predicated (Simon, 1959, 1991). Framing matters for creating influence, but we as a field have drawn the boundaries of our intended influence so nar- rowly that we have unintentionally abdicated our societal leadership responsibilities. A focus on foresight also represents a way of helping to achieve societal influence without the polemics implied in Pfeffer’s (1993) AMR article (a Best Article), which essentially suggests that we should dispense with multiparadigm ap- proaches to organization study so that we can achieve the kind of paradigm consensus associ- ated with other fields that ostensibly have been more successful at garnering resources. An ori- entation toward prescience implies that regard- less of theoretical approach, so long as that ap- proach is attuned to identifying or anticipating theoretically and pragmatically relevant future problem domains, the desired societal influence is more likely to follow. An orientation toward or

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at least a sensitivity to prescience as an at- tribute of theoretical contribution does not merely constitute an addition to a “theory of theoretical contribution”; it also changes the way we think about our traditional notions of contribution itself. Admittedly, this orientation makes the practice of theory generation more challenging because it forces us out of our intel- lectual comfort zone, but then maturation (even as a field) is never an easy undertaking.

Implications for Our Practice

Miller (2007) refers to the “straightjacket” many top-tier journals put on authors that restricts the notion of contribution to “topics that fit neatly within today’s popular theories and allow the de- velopment and tweaking of those theories” (Miller et al., 2009: 278). DiMaggio (1995) notes the extent to which the “cultural resonance” of theories affects their receptivity (i.e., the degree to which a given theory aligns with the cultural beliefs of the time and of the scholarly audience for the theory). As gatekeepers for the most desired and valued out- come in our academic pursuits (published arti- cles), journal editors will obviously have decisive influence on the likelihood any change will be implemented. If the editorial teams of our top-tier journals continue to reward only those papers demonstrating theoretical contributions that are scientifically but not pragmatically useful, little will change in the way authors practice the devel- opment of theory. We have experienced this in our own attempts to focus our theory development on the pragmatic aspects of a phenomenon, as evi- denced by the following reviewer comment con- cerning one of the authors’ recent manuscripts that attempted a melding of academic and prac- titioner voices in the paper: “Your narrative at times sounded like a practitioner rendition.” Al- though our author’s reply attempted to explain (and perhaps educate) the reviewer on the value of a pragmatic aspect to theory building, it remains to be seen whether this reviewer will be convinced of the wisdom of trying to bring convergence to academic and practitioner views.

If, however, journal editors become more open to contributions that demonstrate originality and scope (scientific � pragmatic usefulness) and encourage these dimensions in guidelines to authors and reviewers, then reviewers will begin to shift how they assess theoretical con- tribution. Authors will then be rewarded for de-

veloping more pragmatically useful (and per- haps even prescient) theoretical contributions to match the shifting expectations of journals. If we do not soon change our scholarly traditions in ways that enhance theoretical relevance to practice and our sensegiving potential to the wider audiences, then we will continue to un- derperform our adaptive role in society and con- demn ourselves to increasing irrelevance and diminishing influence in describing, explaining, understanding, and improving organizations and their management.

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Kevin G. Corley ([email protected]) is an associate professor of management in the W. P. Carey School of Business at Arizona State University and an associate editor of the Academy of Management Journal. He received his Ph.D. from The Pennsylvania State University. His research interests focus on sensemaking and organizing pro- cesses, especially in relation to organizational change and identity, image, identifi- cation, and knowledge.

Dennis A. Gioia ([email protected]) is the Klein Professor of Management in the Smeal College of Business at The Pennsylvania State University. His doctoral degree is from Florida State. Previously he worked as an engineer for Boeing Aerospace at Cape Kennedy during the Apollo program and for Ford as corporate recall coordinator. Current theory/research focuses on the ways in which identity and image relate to sensemaking, sensegiving, and organizational change.

32 JanuaryAcademy of Management Review

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