FIVE

Commentary
Walking on Three Legs

J. RICHARD HACKMAN

HERB KELMAN, one of the most distinguished social psychologists of his generation and now an emeritus professor at Harvard, has devoted the last several decades to developing and testing strategies for ameliorating intergroup conflict. He has not been shy about taking on the hardest problems—the Mideast and Northern Ireland, for example—and he has learned a lot about what it takes to reverse, or at least to contain, the escalation of such conflicts. As much as anyone I know, Herb works productively right at the intersection of theory and practice. So it brings a smile when one reads what he has posted on the door of his William James Hall office:

That tongue-in-the-cheek lament poses the challenge. How have we done at surmounting it in the 25 years since the first edition of this book was published? Has there been discernable progress in developing research strategies that enable theory and practice to inform one another? What now commands the attention of scholars who seek to develop knowledge that is both conceptually sound and of practical use? What obstacles and opportunities are most likely to occupy our attention in the years to come? This commentary addresses those questions, fueled by the provocative essays by Susan Albers Mohrman and Allan Mohrman, Amy Edmondson, and Lynda Gratton.

Where We Have Been

There was real excitement at the previous University of Southern California workshop on this topic, a sense that we were on the cusp of something very important. Some of the intellectual leaders in the field of organizational behavior—people like Chris Argyris, Paul Goodman, Ian Mitroff, Andrew Pettigrew, Stan Seashore, and Dick Walton—vigorously engaged with one another to figure out what was required to conduct research that really would be useful for both theory and practice.

A number of provocative ideas about research directions emerged from that workshop. Although there was a lot of variation around the edges, particularly regarding differences in what is needed for actionable research on organizational design versus individual and group behavior within organizations, there also was real progress in identifying the kinds of research that could help us move forward. For me, the main message of the workshop was that the eventual usefulness of our research would depend jointly on how we frame the problems we address and on what types of products we generate.

Some research problems are paradigm-driven whereas others are explicitly problem-driven. Paradigm-driven problems may indeed add bricks to the wall of scientific understanding, but the knowledge obtained rarely generates conceptual models that are useful as guides for managerial or organizational practice. Problem-driven research, by contrast, risks becoming so focused on the specifics of a particular situation that, even if the presenting problem is solved, the findings add little to general knowledge about how people and organizations operate. The right place to be, I concluded, was somewhere around the middle of the paradigm-problem continuum.

The kinds of research products we disseminate also fall on a continuum, this one ranging from articles that report trustworthy but practice-irrelevant findings to what could be called tasty nostrums for managers. And, once again, the middle of the continuum seemed a good place to be—bulletproof conclusions that are irrelevant to practice are just as unhelpful as catchy concepts that are supported tenuously, if at all, by empirical research. What we needed, I concluded, were neither validated contingency models so complex that no mere mortal could use them to guide behavior in real time nor injunctions such as “create a culture of trusting, entrepreneurial leadership” that leave practitioners scratching their heads about what they should actually do to achieve that high-sounding state of affairs.

I came away from the previous workshop with a renewed commitment to be wary of both ends of those two continua. I realized that merely being in the middle provided no guarantee that a piece of research would contribute simultaneously to theory and practice. Still, the middle regions of those continua did seem to provide a good platform from which to develop the strategies and tactics of actionable research. By the new millennium, I thought, we had a reasonably good chance of demonstrating in our work both parts of Kurt Lewin’s oft-cited dictum—that there is nothing so practical as a good theory, but also that there is no better way to inform theory than through a careful analysis of practice. Even better, others at the workshop appeared to share my optimism. It was a heady time.

Where We Are Now

The promise of the previous book has not been fulfilled. Indeed, there are some signs that we may actually be moving in the opposite direction, and I find myself having to marshal my emotional resources to keep from getting depressed about future prospects for actionable research in organizational behavior. Here are three developments that worry me:

1. There is as much variation in research approaches as ever—indeed, probably more—but alternative approaches are less in contention with one another than before.

The field of organizational behavior has prospered in recent decades, with increasing numbers of researchers conducting studies on an ever-expanding set of questions. It probably was inevitable, therefore, that subgroups of researchers would form whose members rely on similar methodological strategies and refer mainly to one another. Although some scholars do identify with multiple subgroups, there is less variation within subgroups than between them—a development that would generate a respectable intra-class correlation but that also attenuates how much the various stripes of organizational researchers learn from one another.

We have, for example, the JPSP crowd. We have other researchers whose fondest dream is to land an ASQ article. And there are still others for whom a piece in HBR would be the ultimate achievement. It is not so much that members of these subgroups disparage one another (although that occasionally does happen), it is more that they ignore one another. Because the informal subgroups that have emerged in our growing field provide ample opportunities for social comparison, peer recognition, and the development of methodological advances, there is little need for members of any one subgroup to engage with scholars from other groups who prefer different research strategies.

For what I am calling the JPSP crowd, for example, collegial exchanges are likely to focus mainly on ways to refine and improve strategies for experimentally testing social psychological theories in controlled laboratory settings. There is no particular need to examine the phenomena being studied as it exists in the wild or to debate methodological approaches with those who carry out their research in field settings. Field researchers, for their part, do need to manage relations with other groups, but those interactions more often are with gatekeepers and managers in the organizations where the research is conducted than with researchers in other subgroups who rely on different methodological strategies. And those whose main audience is practicing managers may interact mainly with the editors of practitioner-oriented books, journals, and magazines in figuring out how to make their work as accessible, engaging, and informative as possible for those readers whose behavior they hope to influence.

Yes, in describing these three subgroups I have caricatured them a bit. And yes, many researchers, including those present at this workshop (and assuredly the authors of the papers about which I am supposed to be commenting), strive mightily to transcend the boundaries of their “home” subgroups. But I stand by my main points—that organizational researchers increasingly are sorting themselves into moderately homogenous subgroups defined by preferred research strategy, that these subgroups are not in intellectual contention with one another, and that those two developments portend poorly for the development of fresh paradigms for the design and conduct of research that contributes simultaneously to theory and practice.

2. The real players in management research and education are not here—they are playing other games on different fields.

The action these days is not in what I will call old-style organizational behavior, which sought to identify the factors that most strongly affect individual and group behavior in organizational contexts and to analyze the forces that shape the dynamics and development of whole organizations. These days, the real action is in fields such as social cognition, judgment and decision making, behavioral economics, and social network analysis. Those who work in these areas know that they are onto something significant, and their optimism and excitement is just as palpable as it was a quarter century ago for old-style organizational behavior researchers (a group with which, in case there is any doubt, I identify myself).

That’s not the problem. Research topics and paradigms come and go, and anyone who resists will be left behind and should be. Scientific understanding moves forward in a slow, amoeba-like way: As the world changes and new issues become fashionable, one pseudopod expands, another one atrophies, and only relics keep on with what they’ve always done. The real problem is this: Concomitant with the changes in fashion has come a migration of the researcher population. Back when the predecessor of this workshop was held, organizational behavior was firmly situated in management schools, with strong two-way links to psychology departments (especially social psychologists) and sociology departments (especially organizational sociologists). Both organizational and discipline-focused scholars had to contend with the views of colleagues whose skills and perspectives differed, sometimes in fundamental ways, from their own.

No more. My colleagues in sociology tell me that the center of gravity for research on “macro” organizational issues is now in management schools. And I know from personal observation that the same is true for “micro” organizational behavior: No psychology department of which I am aware has an active research program in organizational psychology. Moreover, many management schools are recruiting young faculty who identify mainly with the disciplines in which they were trained and who seek most of all to publish in first-rank disciplinary journals. Indeed, more than a few universities are creating what is, in effect, a second social psychology faculty (and, perhaps less frequently, a second sociology faculty) in their professional schools—especially in management but sometimes also in education or government.¹

So once again we see movement toward increasingly homogeneous groups whose members need not be in intellectual contention with other groups about conceptual and methodological problems and paradigms. Even more worrisome is the assumption by some discipline-oriented scholars in management schools that first-rate scholarship can be done without either personal immersion in the phenomena under study or explicit attention to the organizational contexts within which those phenomena unfold. For organizational research that aspires to guide practice, that assumption can be fatal. Scholars who are members of organizational behavior groups in professional schools surely ought to know at least a little about organizations, a little about behavior, and perhaps even a little something about what it takes to conduct research that can contribute simultaneously to theory and practice.

3. The siren song of “applied behavioral science” is getting louder, and many organizational scholars are finding it hard to resist.

“Applied” is one of my least favorite words—especially when it is used to modify the word “psychologist,” and most of all when those two words are joined to describe me. I object because the connotation is that over there is basic science, over here is the real world, and applied psychologists (merely) bring the former constructively to bear on the latter. My aspiration, consistent with the theme of this book, is to generate fundamental knowledge about social phenomena that is directly useful to those who lead or serve in groups and organizations. I don’t want to be just a knowledge carrier.

But my one-person battle against “applied” is not going well, and it is starting to look as if dignified surrender may be my only realistic option. Perversely, it is the constructive efforts of some of my most admired colleagues that are doing me in. Taking their lead from the field of medicine, a number of intellectual leaders in organizational behavior are making a strong and persuasive case for “evidence-based management.” What we should do, the argument goes, is to identify those basic research findings about management practice that are most robust and reliable, compile and package them in a way that makes clear their implications for practice, and then disseminate them widely throughout the management community. That is what is being done in the medical sciences, and evidence-based medicine apparently does help physicians make good treatment decisions—and, most important, it can steer them away from choices that may seem right but that actually are unsupported by empirical research.

The problem, of course, is that it is quite a distance from the laboratory bench to the physician’s consultation room, and neither the laboratory researcher nor the clinical practitioner is likely to have the time or inclination to bridge that gap. So a new medical field, called “translational medicine,” has developed, with the specific objective of making trustworthy findings from medical research available to, and accessible by, practicing clinicians.

Can this also be done for management research? It is an attractive possibility. Basic researchers can proceed with their work without having to worry about its possible usefulness. Practitioners can do their jobs without wondering if there is anything in the scholarly journals that they need to know. And the translators will bridge those communities—extracting, aggregating, and disseminating the most trustworthy and high-leverage research findings.

What is wrong with this picture? What is wrong is that evidence-based management, by abstracting scholarly work from both the contexts where it is conducted and the settings where the findings will be used, takes us one additional step away from the Lewinian ideal of action science. There are so many advantages to action science that I am going to defer my surrender for as long as I can. And, from their chapters, I’m guessing that Susan and Allan, Amy, and Lynda will join me in what may be—but I hope will not be—a last stand against the offense being mounted by the Division of Labor in organizational research.

Where We Should Be Going

This commentary has been mainly about those aspects of contemporary organizational research that make it hard to conduct research that contributes both to basic knowledge and to managerial practice. The difficulties—but also the opportunities—are evident in the chapters in this section of the book. Susan and Allan reflect insightfully on their struggles to overcome the epistemological and collaborative challenges they faced in working with organization-based colleagues to properly design problem-focused research, to conduct it efficiently, and then to report the findings in a way that would be useful to all. Collaboration also is a central theme in Amy’s chapter, especially as scholars cross organizational and disciplinary boundaries to triage research possibilities and then pursue those that show the greatest promise of generating learning for all parties. And Lynda recounts a multiyear, multiorganization program of consultation that started with a relatively straightforward analysis of what it takes to foster cooperation in organizations, but then evolved in ways that could not possibly have been anticipated or planned for in advance. All three chapters demonstrate convincingly that problem-focused research in organizations takes on a life of its own and therefore requires an unusual measure of initiative, flexibility, and creativity by those brave enough to plunge in without knowing for sure where they will wind up.

Even so, it may be that some minimum conditions must be met if organizational research is to have a reasonable chance of both solving real problems and contributing to basic knowledge. Consider the triangle shown below. Its vertices are (1) the phenomena of interest, (2) theory about those phenomena, and (3) empirical research on those same phenomena. I propose that research of the kind we have been discussing must include work on all three of the legs that connect those vertices.

Some scholars, including some discipline-oriented social psychologists (the “JPSP crowd” mentioned earlier), emphasize in their work the first leg of the triangle, the one linking theory and empirical research. Others, such as some business school faculty, emphasize the second leg, inductively developing theory based solely (or mainly) on deep immersion in the phenomena. And still others, such as some “applied” researchers, emphasize the third leg, bringing empirical data to bear on specific problems without worrying too much about conceptual issues.

It is probably asking too much to expect that any one researcher, or even any one research group, will be able to work all three legs of the triangle. The chapters in this section strongly suggest that the development of basic-but-actionable knowledge requires multiple researchers, multiple projects, and no small measure of calendar time. It also will require overcoming, or at least circumventing, several self-imposed barriers that historically have slowed our progress. We will need to quit acting as if writing about the lessons we personally learn from case studies or consulting assignments is, by itself, scholarly work. We will need to quit pretending that the context of behavior is irrelevant to understanding what is happening—let alone to changing it. We will need to become more inventive in developing research strategies that are uniquely suited to our research settings. And then maybe, just maybe, we will no longer find ourselves characterizing our scholarly work as merely “applied” research.

ABOUT THE AUTHOR

J. Richard Hackman is Edgar Pierce Professor of Social and Organizational Psychology. He received his bachelor’s degree in mathematics from Mac-Murray College and his doctorate in social psychology from the University of Illinois. He taught at Yale for twenty years and then moved to his present position at Harvard. Hackman teaches and conducts research on a variety of topics in social and organizational psychology, including team performance, leadership effectiveness, and the design of self-managing teams and organizations. His most recent books are Senior Leadership Teams: What It Takes to Make Them Great (with Ruth Wageman, Debra Nunes, and James Burruss) and Collaborative Intelligence: Using Terms to Solve Hard Problems. He serves on the U.S. Intelligence Science Board and on the Board of Trustees of the Orpheus Chamber Orchestra.