My view is that management research should be primarily phenomenon driven. In other words, I believe the most interesting contributions arise when researchers identify contemporary phenomena that need explaining, or empirical evidence that is inconsistent with existing theories. The academics who influenced my thinking twenty years ago – Joe Bower, Bob Burgelman, Henry Mintzberg, Sumantra Ghoshal – all seemed to espouse this point of view, and it has served me well throughout my own career.
To make the point in a slightly different way, when doctoral students tell me they have identified a gap in the literature or in a body of theory, I become somewhat suspicious, and I push them to justify their claim. Occasionally, I find they are onto something. But more often than not there was either no gap in the first place (it was actually a gap in the understanding of the student!), or the gap was so trivial that it was not worth filling. We certainly need to stay abreast of our colleagues’ work to be good management researchers, but the ‘literature’ is rarely a good place to seek inspiration. Instead, I encourage my doctoral students to get out into the real world – to observe what managers and companies are actually doing, and to iterate back and forth between phenomena and theory.
To avoid misunderstanding, let me clarify two points here. First, I admit there is room in our field for a few pure theorists – people who push their thinking forward through deep introspection or through models or simulations. But we don't need very many of these people, and in addition this is difficult research to do well, with the bar for publishing theory papers getting higher all the time. So I would be unlikely to recommend this track to a doctoral student or junior scholar.
Second, I realize that good research papers are typically motivated by identifying and filling a gap in the literature. However, this is typically a rhetorical exercise – it's a way to craft a paper, to defend a line of argument, and to help the reader contextualize the paper's findings. And in my experience the way a paper ultimately gets framed bears little resemblance to the original logic for conducting the research in the first place.
So what are the types of phenomena that we should be focusing on in our research? Let me suggest three.
First, there are cases where we see a mismatch between theory and practice. For example, my doctoral thesis (Birkinshaw, 1995) was a study of ‘initiative’ in the foreign subsidiaries of multinational companies. The academic literature said, essentially, that subsidiaries existed to follow the orders of their parent company. My interviews with subsidiary managers in Canada showed that they often ignored those orders. It was as simple as that – a disconnect between what I was experiencing in the field and what I was reading in the literature – and it allowed me to develop a series of papers documenting and explaining the mismatch.
Second, there are contemporary phenomena emerging before our eyes that need to be explained. Technology is changing how work gets done: how we coordinate our activities, how we make decisions, how we motivate our colleagues. Social change is bringing a new generation of employees into the workforce, often with very different expectations and motivations to the previous generations. Economic and political changes are bringing new competitors into established markets, often with very different business models and governance structures. And so on. In studying these phenomena, we sometimes discover that they can be adequately explained using existing theories, and we sometimes discover that our theories need adapting. Either way, we are making progress. The Open Source Software movement, for example, has spurred a number of very interesting studies about the nature of collaboration and motivation under different modes of governance (e.g. Benkler, 2002; von Hippel and von Krogh, 2003).
Third, I would point to the increasing acceptance in the management research community for experimentation, as a way of creating or exploring our own phenomena. Controlled, lab-based experiments have been a staple of organizational psychologists for years, but increasingly we are seeing field experiments and quasi-experiments being conducted and written up in the management journals (e.g. Boudreau et al., 2011; Sorensen et al., 2010). In my view this is an important development – it takes very seriously the notion that ‘in order to understand something you have to try to change it’ and it also helps us to advance our understanding of cause-and-effect. Of course, it brings its own challenges, not least the technical skills needed to conduct and write-up a proper field experiment, but as one of many ways forward I think it has enormous merits.
I see two particularly promising directions. One is mainly methodological, the other paradigmatic. Neither requires field redefinition, more a steady turn. Together they can elevate the significance and value of our research.
First, we need more field observation. With some notable exceptions, as management and organization researchers we expend a tiny proportion of our energies actually observing the phenomena we want to understand. Scholars in other sciences ‘get their hands dirty’ by watching, probing, living with – scrutinizing via direct sensory contact – their subject matter. In contrast, the bulk of management research subsists on analysing regularities in statistical surrogates and drawing inferences from self-reports that are often twice removed from the action. The benefits of close contact are many; not least insight, inspiration, curiosity, and ecological validity.
When my colleague and I reviewed the literature on cognition in organizations (admittedly a selective sample of the overall field), we commented that most studies were actually of cognition in the lab rather than cognition in organizations (Hodgkinson and Healey, 2008). I found this surprising, not least because field observation has given us some pivotal moments. It is easy to forget that field ethnography in 1934–35 laid the groundwork for Simon's (1947) specification of bounded rationality (see Simon, 1978). His observations of decisions made by administrators of Milwaukee's public recreational facilities, coupled with a contrasting infusion of psychological and economic theory, led to his discoveries of the centrality of problem representation, satisficing, and so on. Unsurprisingly, Simon (1978, p. 347) was critical of trying to understand organizations ‘without stirring out of our armchairs’. Fast-forward more than half a century to another breakthrough: Hutchins’ (1995) analysis of organizations as naturally situated or socially distributed cognitive systems. The type of cognitive ethnography he pioneered when studying naval navigators in the wild is the most under-utilized tool in organization science. (Note that Hutchins’ research was also exceptional because it combined observation with other methods, notably computer simulation.)
The second opportunity I see rests on a key proposition: singling-out descriptive theory as the sole desideratum of management and organization studies is insufficient for the field's future viability. Given the above comments concerning the derivative nature of management and organization theory and the relative power of explanations from foundational disciplines, our own explanatory products may forever be pale and restricted. Instead, I think we can steal a march by focusing on design. In 2004, Bill Starbuck explained why he had stopped trying to understand the real world and started to try to change it (Starbuck, 2004). He believed that organizational systems are too complex to comprehend using current research methods. His idea was that an organization science rooted in design might not only produce better social realities but also yield better understandings.
Obviously, design approaches have a long history in management and organization research. But progress has been slow on many fronts (Daft and Lewin, 1990; Dunbar and Starbuck, 2006). I think we need to push much harder with the logic that the decisive test of research is not necessarily description, explanation, or even the prediction of abstract variable relations. Rather, the acid test for our discipline should be the ability of our research to reliably inform the active design of artefacts that ultimately yield new and socially valuable organizational processes and forms. How is it that mainstream management research has had so little to say about how to intervene in some of the most significant organizational events of our time, not least the great recession? Perhaps the simple answer is that we have stopped trying to answer questions about organizational design and rarely undertake the type of experimentation that Julian outlined. It is time to restart.
I'm not suggesting here that we give up on theory. My point is that beginning with questions of design – or at least not relegating them to an afterthought – can lead to different kinds of theory. For instance, management theory that provides so-called technological rules (knowledge that links interventions or artefacts with desired outcomes; see van Aken, 2004) differs from purely descriptive theory. Potentially, such types of theory might give our field a useful and distinctive voice. And the value of the design logic extends to areas that have not historically been overly concerned with design, such as strategic management, as much as areas where design is more familiar, such as organizational behaviour.
Now, some may see tension between the logics for observation and design. In fact, the two are natural bedfellows. To illustrate, both the Carnegie School and the situated cognition movement were and are explicitly concerned with design. Much as architects leave their drawing boards to experience notable buildings, getting to know interesting organizations and their activities can inspire design-orientated management research. Doubtless, design knowledge and ethos can enrich observation too.
Karl Popper (1963) once said that disciplines are not distinguished by their respective subject matter but by the problems they define. A greater emphasis on observation and design can improve how we define and approach problems in management research, and in so doing help to secure a valued and enduring identity for the field.
I see three clear ways in which we, as a profession, can maintain a healthy balance between developing indigenous theory and remaining open to ideas, methods, and frameworks from adjacent fields. The first path is to maintain a clear focus on management and organizational phenomena. Julian and Mark have already provided an outstanding articulation of this argument, and I have nothing to add to their insights. The other two strategies are equally important and deserve some elaboration. One is to expand our definition of ‘foundational’ knowledge beyond the scientism represented by economics, sociology, and psychology to include arts, literature, and philosophy. The second is to become more self-reflexive about management scholarship by embracing, protecting, and teaching our scholastic history. I elaborate each of these points.
Foundations for management knowledge. I think we need to be careful, as a discipline, to avoid using the rhetoric of openness to promote a narrow view of what constitutes management scholarship. Typically, critics of the notion of indigenous management scholarship point to the ‘foundational’ paradigms of economics, sociology, and psychology as the primary source for importing ideas and methods to organizational research. Critics within each of these disciplines, however, have argued that, over time and in the pursuit of scientific objectivity, these disciplines have narrowed, become fetishistic about quantitative methods, and have become increasingly divorced from their core phenomenal reality (see McClosky, 1994 for economics; Guthrie, 2004 for sociology; and Bannister, 1987 for psychology).
As well, each of these disciplines has developed their own imperialistic tendencies to construct paradigmatic boundaries that seem to impede the movement of knowledge between disciplines and across levels of analysis. I often wonder if our devotion to these three, and only these three, founts of knowledge have contributed to our own inability to effectively produce multi-level studies of organizations, the growing gap between macro- and micro-level studies of management, and the ongoing complaints about our inability to address issues of importance to practitioners.
If our interest is to expand our understanding of organizations and management by drawing on a wide array of outside knowledge sources, why do we typically restrict ourselves to these three disciplines? Surely we could also look to literature, philosophy, history, political science, and related subjects in the humanities to frame our scholarship. For many decades scholars have decried the overemphasis of science, at the expense of the humanities, in management education (Bennis and O'Toole, 2005; Gordon and Howell, 1959; Mulligan, 1987; Pierson, 1959; Zald, 1996). I note, with considerable gratification, a small but encouraging number of studies that adopt methods and theoretical lenses from the humanities to gain insight into managerial phenomena. These studies demonstrate that we can learn something about business strategy by studying the history of the fall of Rome (Carmelli and Markman, 2011), or learn something about organizations by analysing the rich ethnography represented in the television drama The Wire (Zundel et al., 2013). As Meyer Zald (1996) noted some time ago, we have a lot to learn from the humanities, particularly about the use of interpretive methods and treating the subject of our inquiries as particularistic wholes rather than objective abstractions. What Zald identified as unexploited back in 1996, and which remains unexplored today, lies at the intersections of organization theory and history, literary criticism, and philosophy.
So one clear way forward for management to balance the need to develop a distinctive voice while being open to other sources of knowledge, is to broaden our definition of openness to include the humanities, both as a source of interpretive methodology as well as a resource for new theoretical frameworks. Embracing the humanities will, I think, serve as a useful check on the dangers of importing the fetishes of scientism. More importantly, it will sensitize researchers to the view that the phenomenal elements of management and organization, indeed their more interesting aspects, often extend beyond the reach of scientific objectivity.
Self-reflexivityAnother solution is to encourage greater self-reflexivity about our profession. In part this means making more time and space for debates and discussions like this in our professional journals. But it also means devoting more time and paying more attention to our own history as a profession. Understanding our own history is important, not only for developing a distinct professional identity – medicine, law, engineering, and most other professions are very attentive to the history of their scholarship – but it is critically important to overcome the false belief that our knowledge base is not historically contingent.
One of the perverse outcomes of scientism is the erroneous assumption that our knowledge is objective – i.e. that it transcends time and space and that new knowledge builds inexorably on prior knowledge, as it might in the physical sciences. This misunderstanding, in turn, is built on the related misassumption that our knowledge does not affect the objects of our study – i.e. that managers do not learn and adapt their behaviour because of our research.
We know, however, that this is simply not true. The standards and practices of pursuing competitive advantage change as our knowledge of, for example, generic strategies, technological lockout, and valuable, rare, and inimitable resources, diffuses to practising managers. Similarly, our knowledge of options pricing actually changed substantive practices in financial markets. In contrast to the physical sciences, the objects of inquiry are significantly changed as our knowledge diffuses. Not only does this create an ongoing cycle of new knowledge creation and diffusion, it makes our knowledge historically contingent and reinforces the need to understand the history of our scholarship and its effects.
Yet we have few institutionalized mechanisms within our profession to reinforce the historically contingent nature of our knowledge. We typically do not teach the history of management theory to our graduate students. Most graduate course syllabi that I encounter tend to offer but a few honorific references to the ‘classics’ while privileging more recent studies. I am not aware of any business school that offers an entire course to the history of management thought or that explicitly addresses the historically contingent nature of our scholarship. Without this degree of self-reflexivity, where we not only celebrate our historical identity as management scholars, but also contemplate its implications for our knowledge base, we will likely fail to ever generate any indigenous theory.
In sum, I am very, very optimistic about the future of management scholarship. We need to remember that, as a distinct discipline, we are still very young. Our senior colleagues can likely still remember when business schools first became legitimated in the latter half of the twentieth century (and were rapidly populated by importing staff from the ‘foundational’ disciplines described above). We are now moving into the ‘second generation’ of management research. Hopefully this new generation will bring with them a degree of openness, self-reflexivity as a discipline and a very broad minded attitude about the scope of the field.
The strong suit of management and organizational scholars is building mid-range theories grounded in observation of the world around us. As a community, we are not very good social theorists, and poor philosophers. The reason is simple: we concern ourselves with – in the grand scheme of things – a fairly narrow set of phenomena, namely formal organizations, almost exclusively in commercial contexts, during a relatively short historical era, and mostly in market economies of Western democratic societies. It is difficult to build grand theories from a narrow base of phenomena. The somewhat limited range of empirical settings is also a main reason for why connecting with other disciplines is so important. The ability to compare and borrow from theories and phenomena developed for different purposes sharpens our understanding of management and encourages creativity.
To clarify, developing mid-range theories of a limited domain of social life is a good thing. ‘Small theories’ provide a flexible toolkit to confront the complex and shifting realities of organizations and their management. More pragmatically, that focus is also due to the institutional context of management research and hence hard to change. Much of contemporary research on management is housed in business schools and management departments, where researchers teach primarily practising and aspiring managers of for-profit firms. And I do believe that as a field, management studies has become quite good at the craft of theory building – the process of theory building from data has become more rigorous without becoming overly formalistic or purely mathematical.
Perhaps in contrast to some of the other contributions to this debate, I believe that our efforts should continue to be aimed at theory development. Our understanding of organizations and management is far from complete or conclusive, and as students of social processes, we are working with a moving target. As academics with a commitment to methodological rigour, we are also not nimble enough to simply report on new phenomena, a task I believe we should leave to consultants, journalists, and think tanks. The unique role of academic scholarship in societal knowledge systems is to systematize, memorize, stabilize, and abstract. That means that it is quite natural and appropriate to not always have a conclusive view about a specific event or timely phenomenon. We should study fads and fashions, not chase them.
The implication of this role of academic management scholarship, and its current anchor in studying for-profit organizations, is that to develop our theories and contribute to the public good, management scholars should expand the range of phenomena studied, with a view to advance theory by doing so. I see a particular need to (re-)engage with organization and management in other sectors, geographies, and eras, and to study these phenomena from the vantage point of different stakeholders and participants. Encouraging recent examples are calls to study development NGOs as organizations (Watkins et al., 2012), to pay attention to organizations and markets in informal economies (Bruton et al., 2012), to re-engage with management in the public sector (Kelman, 2007), and to study new forms of production and market exchange in cross-sectoral hybrid organizations and in communal systems such as open source development or crowd sourcing (Afuah and Tucci, 2012). A similar argument can be made about theories that take the perspective not of managers or firms, but of consumers, workers, and social stakeholders that engage with organizations; an example are theories of deliberative democracy as a form of coordination among stakeholders with unequal power and divergent interests.
These are areas in which the theoretical and analytical toolkit of management scholarship can also contribute new insights. For example, Watkins et al. (2012) convincingly show that economic development research has not taken seriously the organizational nature of the agents involved – NGOs, funding agencies, governments – and may hence have ignored important dynamics when arriving at policy conclusions about the most effective delivery of development assistance. A good example of how organization and management theory can contribute significantly to other areas of studies is social movement research in sociology. Resource mobilization theory dramatically changed social movement research by treating movements as organizational fields and applying organizational analysis to movement dynamics (McCarthy and Zald, 1977; see Weber and King, forthcoming, for a historical review).
Equally important, however, is that such engagement with new phenomena is used to question, sharpen, and extend existing mid-range theories of management and organizations. Management theory will benefit from a more comparative approach that keeps a check on the urge to over-generalize from a narrow range of phenomena. In addition to a scholarship of discovery that studies a wider range of things, this implies an equal need for a scholarship of integration that synthesizes, reviews, and classifies phenomena and theories. Attempts at mid-range (vs. narrow range) theorizing can serve as the glue and discipline that keeps an eclectic field together and a friendly alternative to paradigmatic closure. The emphasis here is on ‘attempt’ – process – more than the success of such attempts. In sum, management and organization scholarship will benefit from increasing requisite variety in the form of diverse objects of study and from increasing integration in the form of engagement and generalization across topics and theories.