Useful Research

Advancing Theory and Practice

Susan Albers Mohrman, Ed Lawler, Ed Lawler

• Publisher: Berrett-Koehler Publishers
• Year: 2011
• eBook ISBN: 9781605096025
• Edition: 1
• Topic: Business
• Subtopic: Operations
• Index: Business

Features a who's who of leading management scholarsTakes a stand on a major controversy in academia: should organizational research aspire to be relevant to practitioners?A sequel to the seminal book, Doing Research That is Useful for Theory and Practice, also edited by Ed Lawler, Susan Mohrman, and Associates For decades there has been an ongoing, at times heated, debate over how relevant to real-world organizational concerns academic organizational research should be. The contributors to this book argue that in order to keep organizational research relevant to both theory and practice, research must deviate from the orthodoxy of traditional positivistic research. The true test of whether knowledge is useful to practice is not whether it is "theoretically" impactful but whether it is theoretically impactful and results in improved organizational effectiveness.The contributing authors were selected for their demonstrated ability to conduct useful research and their distinguished academic careers. Part I of the book features active scholars who describe the choices they make and the tactics they employ to ensure that their work advances both theory and practice. In part II, four highly respected researchers reflect on how they approached their careers so that they could have a broad impact on practice and still maintain academic rigor. Part III describes pathways to bring academic knowledge to practice—working with consultancies, executive PhD programs, OD specialists, and professional associations, as well as framing academic concepts in ways that are attention-grabbing, memorable, and credible to practitioners. Part IV looks at institutional constraints and enablers: the prospects for useful research in traditional academic settings like business schools, peer-reviewed journals, and the Academy of Management. Finally, part V sums up the themes of the book and the challenges and opportunities facing researchers who aspire to do research that advances both theory and practice.Contributors: Jean Bartunek, Michael Beer, George Benson, John Boudreau, Wayne Cascio, Thomas Cummings, Amy Edmondson, Lynda Gratton, J. Richard Hackman, Gary Latham, Phillip Mirvis, Allan M. Mohrman, David Nadler, James O'Toole, C. K. Prahalad, Denise Rousseau, Sara Rynes, Edgar Schein, Ramakrishnan V. Tenkasi, Michael Tushman, Andrew Van de Ven, Ruth Wageman, Ian Ziskin

PART I


Exemplars of Useful Research

TWO

Crossing Boundaries to Investigate Problems in the Field
An Approach to Useful Research

AMY C. EDMONDSON

FOR MOST SCHOLARS in organizational behavior, the importance of advancing theory is obvious. In a field that arose in response to management challenges (Miner, 2002), one might argue that research advancing practice should be highly valued as well. Indeed, the need for strategies to manage the challenges faced by the organizations that inspire and fund our work creates an obvious imperative for research that helps those who manage and work in them.

We are told that the norms and demands of academic careers limit our ability to be useful (e.g., Fox, 2003). As the scholars in this book illustrate, however, the hurdles are far from insurmountable. Perhaps the dichotomy between theory and practice need not be so pronounced. Indeed, many of us draw inspiration from Kurt Lewin (1945, p. 129), who argued, over a half century ago, “Nothing is as practical as a good theory.” In this well-known statement, Lewin was not claiming that theory, by its very existence, is practical and should be respected as such, but rather that a good theory is one that can demonstrate its claim. As Lewin’s student Chris Argyris (e.g., 1980, 1982, 1993) has argued tirelessly, this is a tall order, but one that management researchers must embrace if we are to make a difference in the world. Though few journals appear to seek out or publish work with a practical component, the tradition of action research has remained vital and inspiring over the intervening decades (e.g., Argyris, Putnam, & Smith, 1988; Clark, 1980; Fox, 2003; Schein, 1987; Schwarz, 1994).

What drew me to the field of organizational behavior twenty years ago was exactly this opportunity—to engage in research and teaching aimed at understanding and informing practice. Yet those just starting research careers might be well advised not to read on. The approach I describe in this chapter—starting with problems, going out into the field, and reaching across boundaries of several kinds—is almost certain to slow you down and may even harm your career. (Of course, I hope not, and I don’t believe it to be true. But many do, and so I offer this reluctant caveat as an invitation to help challenge it.)

This chapter presents experiential reflections rather than systematic analyses. I did not conduct a literature search to identify and analyze useful studies so as to determine what they have in common, but instead reflected on my own research activities over the past two decades to consider what factors have been most instrumental in tying me to practice. I did not need to be convinced to pursue practical knowledge. This aim was embedded in my long-standing sense of purpose. Coming from a family of inventors and engineers, I began the study of organizational behavior in the early 1990s with a deep bias toward the pursuit of the practical. A decade earlier, in my first job after college, I worked as an engineer for Buckminster Fuller, designing and building geodesic domes for uses ranging from food production to emergency shelter. Fuller—a college dropout from the Harvard class of 1917 and at the time an internationally known inventor, architect, and author—was the perfect mentor to reinforce my bias against further academic endeavors. Drawing from these family and early career influences, I had been certain that making a difference in the world did not involve time out for graduate school. Furthermore, at that time, I was not yet aware of the field of organizational behavior.

What happened to change my course from applied engineering to organizational research? To begin, while working with Fuller, I led the occasional team in the construction of full-scale geodesic prototypes, sparking an initial, but still largely dormant, interest in organizational dynamics that affect collaborative work. After Fuller’s death in 1983, I wrote a book about his mathematical concepts (Edmondson, 1987) but remained mute on his efforts to inspire and engage people in work that made a difference in the world—ideas well captured by others (e.g., Baldwin, 1996; Kenner, 1973). It was not until a few years later, working for a small consulting firm that helped managers implement change programs in companies, that I became aware of the need for better knowledge about the design and management of organizations. In that job, I spent many hours interviewing and observing in large companies as varied as General Motors and Apple, obtaining the beginnings of an education in organizational behavior. I decided to apply to graduate school at the point when I realized that my ignorance in psychology, management, and business was limiting my usefulness in these settings.

As a doctoral student, however, I soon found that usefulness was not at the top of the list of criteria with which scholars evaluated research in organizational behavior. Discovering the predecessor to this book, Doing Research That Is Useful for Theory and Practice (1985), thus had been profoundly reassuring. The essays and dialogue among so many of the field’s leading researchers—Chris Argyris, Paul Goodman, Richard Hackman, Ed Lawler, Dick Walton—made it clear to me that an aspiration to develop practical knowledge in organization studies was consistent with the purpose of the field.

Reflecting on how this quest has played out in the past two decades in my own work, I identified three attributes of my approach to conducting research that may increase the chances of the research being useful: starting with an important problem, getting into the field (early and often), and not being afraid to collaborate across disciplinary and organizational boundaries. Although of dubious merit as a theory of relevance, these elements are likely to increase the chances of stumbling into useful knowledge and almost certainly make the research journey more interesting.

Three Elements of Useful Research

Start with Problems

Problems provide a natural connection with practice. Studying a compelling problem, researchers are motivated to care about action. Problems matter! They matter to actors in the field coping with them, of course, and those reading one’s work are likely to find them interesting as well (Fox, 2003). As compelling as publishing articles for scholarly colleagues may be, research that might help solve a problem in the world is usually that much more so.

The problem with problems is, of course, their apparently low status as “applied” research (Fox, 2003; Greenwood & Levin, 1998). And, problem-driven research brings additional risks to scholars. First, the work might turn out to be mundane if it merely addresses a problem that seems important to practitioners but uninspiring to other scholars. Second, problem-driven research risks rediscovering the obvious or generating pragmatic but situation-specific recommendations. Theory-driven research, in comparison, is awarded higher status and is believed to be more general and enduring (Fox, 2003). I nonetheless argue that problems open doors to new ideas and new theory. Starting with an important problem does not mean one must solve it single-handedly but rather that one can use it as a lens with which to investigate an organizational phenomenon that has importance for practices as well as for theory. Starting with a problem does, I believe, call for at least interest in solutions, as well as for empathy for those who face the problem.

One obvious reason that research motivated by problems might increase its usefulness is that efforts to understand a problem are likely to trigger ideas about how to solve it. Occasionally, solutions to problems can be investigated, tested, or refined, whether in the same or in subsequent research projects (Clark, 1980). More subtly, problems may facilitate the production of useful research because real problems in organizations are complex and multifaceted, provoking consideration of issues beyond those that motivated the study in the first place. In contrast to theory-driven research, which often remains tightly focused—adhering to a specific research framework and design—problem-driven research may sometimes follow the trail of problems where it leads. Lateral thinking about issues related to the initial problem then may trigger ideas for practice as well as new ideas for theory. Perhaps most important, developing knowledge about a problem builds the depth of understanding that makes the solutions researchers or their organizational partners might design more likely to work.

A study of errors

To illustrate, medication error in hospitals is an example of a real world problem. Motivated by research interests in both organizational learning and workplace safety, in the early 1990s I joined a team of nurses and physicians in an in-depth study of medication errors in hospitals. The team was organized to collect data to measure error rates in a dozen or so hospital units (work groups that provide patient care) in two hospitals with attention to potential organizational causes of error. I thus joined the team with a narrow research question: Did better teams make fewer errors? My design would predict the team-level error rate (being assessed by data on medication errors to be collected by clinicians over a six-month period) with data on team design, team process, and leader behavior, collected during the first month of the study. I used a modified version of Richard Hackman’s team diagnostic survey to measure team properties (Wageman, Hackman, & Lehman, 2005). From a practice perspective, if my main hypothesis was supported, efforts to build stronger unit-based teams might help reduce errors.

The reality of drug errors was more complex than my initial design had considered. Reflecting a risk for problem-driven research in general, the process of digging into the problem of drug errors uncovered a new, related problem. This came to light when my analysis of the painstakingly collected quantitative data produced findings that appeared to be the exact opposite of what I had predicted: Well-led teams with good relationships among members were apparently making more mistakes related to medications, not fewer. There was a significant correlation between teamwork and error rates in what I initially considered “the wrong direction.” This was a surprise—and of course, a puzzle. Did better-led teams really make more mistakes? With what I had learned of the phenomenon already at that point—the many handoffs across caregivers, the need for communication, coordination, help-seeking, and double-checking to achieve safe, error-free care—I did not think it made sense that good teamwork would increase the chance of errors. The opportunity to get into the field, described in the section titled “Strategies for Building Understanding in the Field,” was essential to getting to the bottom of this unexpected result.

Other problem-inspired studies

Although medication errors present a particularly tangible example, organizational problems come in many forms and can motivate a variety of research projects. Other examples from my own work include action research with a senior management team in a midsized U.S. manufacturing company facing declining revenues and profits after a half century of growth (Edmondson & Smith, 2006), a study of the difficulties of changing surgical team behaviors to accommodate a new technology (Edmondson, Bohmer, & Pisano, 2001a), an investigation of inconsistent use of best practices across neonatal intensive care units (NICUs) in North American hospitals (Tucker, Nembhard, & Edmondson, 2007), and a study of speaking up failures in a multinational company (Detert & Edmondson, 2010).

All of these studies were motivated by problems and management challenges that were important to people working in the involved organizations. At the same time, I entered each of them hoping to be able to contribute knowledge to organizational learning research as well. Further, none of these studies produced the findings or theoretical contributions I expected or hoped for at the outset. Although I believe the actual contributions were more interesting than those planned, I am not an objective judge. In any case, the time spent studying the issues that started the projects invariably led to new questions, new insights, and some unexpected contributions to the literature.

For example, at the beginning of our study of a new surgical technology, my colleague, Gary Pisano, wanted to study learning curves in a service setting. As an economist with expertise in manufacturing—particularly in the process innovations involved in the manufacture of complex pharmaceuticals (see Pisano, 1996)—Pisano saw cardiac surgery as a novel setting for investigating learning curves. With a well-developed network in health care businesses, he soon identified a device maker launching an innovative technology for minimally invasive surgery and requested its help collecting data on surgical time for consecutive operations from several of the adopting hospitals. Both the company and the hospitals participated willingly, hoping to learn from the research.

Unexpectedly, in his early conversations, salespeople in close contact with the clinicians repeatedly told Pisano that success with the new technology was all about “the team” and its “teamwork.” These comments made Pisano understandably nervous; as an economist, teamwork was not something he had been prepared to consider, let alone measure. But, my office was next door to his, and soon he had me as a new collaborator. (Richard Bohmer, a physician, also joined the team, a crucial addition, as noted in the section titled “Disciplinary boundaries.”) Together, we shifted gears to include extensive interviews with all members of the operating room teams and others close to the technology implementation efforts in 16 hospitals. Having been led by the sales representatives to study the “problem” of needing a new kind of teamwork to succeed with minimally invasive surgery, we had a new focus to our collaborative research. Indeed, fewer than half of the 16 adopting cardiac surgery departments we studied successfully implemented the technology (that is, they continued to offer the procedure after an initial learning period). Others abandoned the effort, leaving future patients without the option of a less invasive operation and a quicker recovery. As our qualitative data revealed, operating room teams had to figure out new ways of working together to accommodate the new technology, and this proved far from easy.

Similarly, the problem of a weak strategy and deteriorating business results that initiated our action research with the senior management team in the manufacturing company also unveiled a new, different problem for us to study: how to manage emotion-laden interpersonal conflicts in a decision-making group (Edmondson & Smith, 2006). This new problem was of great interest to us as scholars, and the challenge it presented captured the attention of our executive colleagues as well.

Back in the hospital context, when my colleagues and I set out to study best practice implementation teams in the NICU, the perceived problem according to the two physicians who first contacted me was to speed up team learning. But, along the way, a new problem emerged: the state of medical knowledge (the “evidence”) supporting the practices being implemented by the unit-based teams varied widely. With less research evidence of medical efficacy, teams had more difficulty implementing the required changes in their organizations (Tucker, Nembhard, & Edmondson, 2007).

Summary

In each of these projects, problems were helpful for focusing and motivating the research activities. Problems spawned research questions, generated insights and solutions, and most of all, facilitated access to field sites. Without problems, our field-based collaborators would have been far less likely to welcome us into their world, offering us access to data. And, in each case, the initial problem did not tell the whole story of the phenomenon. Field-based research allowed the problems and plots to shift and to thicken.

Go Out into the Field

Unless you have an unusual office location, sitting at your desk is unlikely to be the most conducive situation for gaining insight into the kinds of organizational phenomena previously described. Although one can learn about an industry or company from written materials, fuller understanding and new ideas are more likely when meeting and observing people who work in that setting. Deciding to pursue field-based research also has its risks. One can negotiate access to a site only to have it fall through, or have it not offer the kind of data needed for answering a research question. Moreover, understanding a situation well requires multiple observations, and some interviews or visits do not yield anything useful. Further, as noted in the prior section titled “Start with Problems,” the research question one asks may evolve as understanding of the setting deepens, posing challenges for consistency. In short, the research process can be inefficient, fraught with logi...

Table of contents

• Cover Page
• Title Page
• Copyright Page
• Contents
• Introduction
• One: Research for Theory and Practice: Framing the Challenge
• Part I Exemplars of Useful Research
• Part II Bodies of Work That Have Influenced Theory and Practice
• Part III Pathways: Research to Practice
• Part IV Barriers and Enablers
• Part V Putting It All Together
• Acknowledgments
• Index
• About the Center for Effective Organizations (CEO)
• About the Editors
• Footnotes