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Keywords:

  • management practice;
  • management research;
  • methods;
  • theory

Abstract

  1. Top of page
  2. Abstract
  3. Editors’ Introduction
  4. Looking Forward
  5. Conclusion
  6. References

The Editors of JMS invited four leading scholars in research on management and organizations to have an open discussion on the current state and future prospects of management research. Our four contributors discuss, among other things, the growing influence of economics, psychology, and sociology on current management research, and the danger of an increasingly fetishistic and formulaic approach to management research that they believe may lead to stale and narrow contributions. Such an approach carries a risk in the long run of seriously dampening the intellectual vigour and impact of management research. Our contributors conclude their discussion with a number of recommendations for management researchers. These recommendations include asking bigger, better, and more challenging questions compared to the orthodoxy in our management research and engaging in modes of research that are not only intellectually challenging but that also have the potential of making a real impact on management practice.


Editors’ Introduction

  1. Top of page
  2. Abstract
  3. Editors’ Introduction
  4. Looking Forward
  5. Conclusion
  6. References

To celebrate the 50th anniversary of the Journal of Management Studies and its contribution to the discipline of management studies, we felt it appropriate to take stock of the discipline and to explore future directions and challenges. As such, in this Special Issue devoted to the 50 years of publishing in the Journal of Management Studies, we introduce a unique format for inquiry. In this article, we have four leading scholars debate and provide deep insight into an issue we consider core to the future trajectories of research on management and organizations.

Our motive for initiating this debate is rooted in a simple but important observation. Whilst management research1 has grown in size and significance over the past couple of decades, in tandem with the growing size and significance of business education around the world, the subject also finds itself in an increasingly vexing position. Never before have there been so many researchers writing about management and organizations, and the number of students enrolled on business related courses and degrees across the globe dwarfs student numbers in other disciplines and at other schools. At the same time, there has been a growing criticism of management researchers in their failure to develop a coherent and progressive body of management ideas that can influence and shape practice. To outsiders, such as university administrators and researchers in other parts of the social sciences, it also often seems odd that a discipline that has existed in some form for decades, has not yet managed to resolve the most basic issue of settling on a common theoretical approach and set of methods.

On this last point, it is noteworthy that in recent years research within management studies has increasingly turned for inspiration to other social science disciplines, such as economics, sociology, and psychology. Recent recruitment drives in leading business schools around the world have focused on recruiting sociologists, psychologists, and economists. Doctoral programmes at business schools also increasingly turn to specialist disciplines, such as sociology or psychology (Mudambi et al., 2012), in part as it gives a specialist edge in publishing research and a convergence on methods, but also the ability to draw on a single solid theoretical base. Equally, citation patterns of articles in our leading journals show an exclusive focus on either economics, sociology, or psychology as the backdrop for a study, but with very little integration between these traditions (Agarwal and Hoetker, 2007).

Reflecting these trends, some have in turn labelled the economics, sociology, and psychology disciplines as ‘foundational’ or ‘mother’ disciplines for management research. One could think of many other similar sounding metaphors and descriptions. There is no need to go into detail on any of those labels here, but in essence such descriptions do point to what is, knowingly or not, seen as a future and direction for management studies, a future that actually on closer reflection may have significant consequences, and not all good, for the discipline and likewise for business schools and business education as a whole.

This situation, if it is indeed a fair characterization of current trends, obviously paints a challenging picture for the future of management research. As with other processes of institutional change, it can be difficult to escape the magnetic pull of these trends, particularly when such trends are already manifesting themselves and to some extent becoming a reality in management research. It may also be hard, in the midst of such developments, to get the measure of the real change that is taking place and to have a good sense of the consequences that it will have on management research, as a subject area and discipline in its own right. The debate and dialogue in these pages constitute an attempt at developing a better understanding of these trends and changes, and to confront ourselves as management researchers with the real choices that we have in front of us.

The contributors to this debate probably need little introduction, other than saying that they are all very reputable scholars with vast experience as editors, reviewers, and authors. They have also acted in various leadership and institutional roles within their institutions and in the scholarly community, and may thus have a good sense and overview of the changes and challenges in our discipline. As editors, we did not know at the outset what the exact shape of this discussion would be (nor did we want to influence this too much), but we did ask each contributor to be as frank, detailed, and provocative as possible to push the discussion forward, and to suggest ways in which we, as management researchers, can collectively best approach the broad issues and challenges ahead of us. And obviously, we did as editors sketch the overarching contours for the debate by setting the scene and by asking each contributor to answer the opening question. Following their contributions, we then summarized their main points, and asked in turn for their thoughts and recommendations for what we collectively, as authors, reviewers, and editors, and as representatives of our discipline, can and perhaps should do to bolster the strength and vitality of management research.

We initiated the discussion with these questions:

How do you see the development of management studies within the social sciences more broadly? Why do you think management studies is so reliant on other social science disciplines for knowledge production? Is this healthy? How does this affect the discipline?

Julian Birkinshaw

I think it is right for management studies – as an applied, phenomenon-based field of study – to build on the base disciplines of economics, sociology, and psychology. I am also drawn to the idea that management might develop its own distinctive point of view – what my late colleague, Sumantra Ghoshal, referred to as a ‘managerial theory of the firm’. My bias, in other words, is towards theoretical pluralism. The organizations we study are complex and the activities of management are multi-faceted, so we should use whatever tools and insights we can get hold of to improve our understanding of them.

However, I am still deeply concerned that the field of management studies is being hijacked by the interests of discipline-trained scholars. As many others have observed, scholars trained in one of the base disciplines bring with them a set of assumptions and methodologies that lead them towards rigorous but typically narrow contributions. This is fine up to a point. The problem comes when this type of research ‘squeezes out’ studies that don't conform to those disciplinary norms. And, regrettably, I see quite a lot of evidence that this squeezing out is taking place.

Here is an example: I was presenting some preliminary findings from a large study looking at the relationship between strategic consensus and firm performance, with around 100 respondents spread over multiple managerial levels, in each of 40 business units – 4000 questionnaires in all. The data-collection effort here had been enormous, but my discipline-based colleagues took me to task for the lack of objective measures, the cross-sectional nature of the evidence, the risk of endogeneity, the lack of instrumental variables, and so on. In their minds, these were ‘fatal flaws’ that meant the research shouldn't be published. My response was, if so, we would have to accept that an entire class of research questions simply could not be studied.

This situation is a form of what Philip Selznick called a ‘retreat to technology’. In other words, when faced with a difficult set of trade-offs, the easy option is for individuals to hide behind a wall of technical superiority. If there is a battle (in the review process, in a seminar, in a hiring decision) between strong technical skills and interesting ideas, there is only ever one winner. This has perhaps always been the case – I recall reading Henry Mintzberg's views on this when I was a doctoral student 20 years ago – but I believe the increasing sophistication of the social science disciplines is making the problem more acute.

There is no simple solution here. According to Selznick, the antidote to the ‘retreat to technology’ is leadership – the ‘infusion of value’ in the institution. This means, for example, journal editors taking a more active role in shepherding interesting papers through the review process, senior academics taking on more ambitious projects with their doctoral students, or faculty review committees supporting unusual cases for promotion and tenure. Some of these things are happening, but not with the consistency or scale needed to halt the advance of disciplinary orthodoxy in our field.

Mark Healey

I understand Julian's concerns about the potential effects on management studies of ‘hijacking’ by so-called foundational social science disciplines (e.g. economics, psychology, sociology). And yet, it strikes me that viewing scholars from other disciplines as hijackers, invaders, or colonists may not necessarily be the healthiest way to proceed.

Whether we like it or not, as management scholars we are enmeshed in a wider system of knowledge production. Our theories, concepts, and methods are almost always influenced by our links, implicit and explicit, with knowledge producers in other disciplines. Some of the most important advances in our field are testimony to the fact that such collaboration has proved fruitful. Cognitive psychology inspired Simon's work on bounded rationality. Meyer and colleagues’ neo-institutional theory is rooted in sociology. The resource-based view of the firm owes much to economics. None of these works would have been possible in a disciplinary vacuum.

Unfortunately, as but one part of a knowledge production system we do not hold a monopoly on the study of people, management, and organizations. Other disciplines also produce ideas and insights about these phenomena. Hence, at the same time that we collaborate with other disciplines, we are also in competition with them. In research funding, for example, over the five years commencing 2007/08 the average success rate for applications to the UK's Economic and Social Science Research Council (ESRC) in management and business was 10 per cent, compared to 24 per cent in economics, 21 per cent in psychology, and 19 per cent in sociology. We also compete with other disciplines for the ear of policy makers and practitioners. Often, these stakeholders believe that the big, important ideas concerning management stem from the foundational disciplines. We unwittingly reinforce this impression when we propagate these ideas in our own research. The danger here is that policy makers and practitioners see management research as a derivative field that they can easily squeeze out in favour of direct conversations with the perceived oracles.

Given its sensitive position, the field of management studies faces some seemingly divergent challenges. It seems beneficial, if not inevitable, for its theories and methods to co-evolve with those of adjacent social science disciplines. At the same time, if the field is to survive it must find a means of providing a unique voice on the diverse set of problems it studies, a voice that other social scientists and practitioners/policy makers value. The influx into management of discipline-trained scholars should assist with the process of ‘back filling’ to those disciplines, given their familiarity with relevant disciplinary norms. In the short term, this activity might enhance the scientific legitimacy of management studies. However, in the long term this trend could well undermine the very identity of the field if new scholars skew rewards and practices too far towards those of their parent disciplines.

While the argument for protectionism is appealing, we should not lose sight of the fact that the very thing we are seeking to protect – the field of management studies – is itself changing. As Whitley (2000) observed, the organization of social science is moving away from a system defined by traditional disciplinary boundaries and towards one defined by specialized areas of interest occupied by scholars with diverse skills and backgrounds. The growing subfields of entrepreneurship and innovation illustrate this trend in management studies. As a community of scholars, we need to embrace, not fight against these developments.

Roy Suddaby

I share Julian's sentiments about the absence of an indigenous research agenda for management scholarship. There is a clear danger in importing the agendas, metaphors, and methodological predispositions of other disciplines. Whetten et al. (2009) have written about the intellectual risks associated with importing theory from other disciplines, and Ferraro et al. (2005) eloquently describe how the theories that we use to interpret reality can actually influence the reality that we construct.

I also agree with Mark's concerns about the danger and futility in raising imperialistic flags to stake a jurisdictional claim over management research. We exist in a free market for ideas and good ideas are equally as likely to originate in sociology or economics as they are in business schools.

But the debate between indigenous versus foundational theory masks what I think is a much more serious problem of the degree to which we now emphasize rationalism over empiricism in generating management knowledge. The result, I suggest, is a growing tendency amongst management scholars to be increasingly fetishistic about theory, often at the expense of phenomena.

Let me explain what I mean about fetishistic theory. A short time ago I was asked by the then editor in chief of the Academy of Management Review, Martin Kilduff, to co-edit the journal's decanal special issue on theory. After some discussion we chose as the focal subject of the special issue the question ‘where are the new theories of organization?’ We chose this question based on the observation that while the world of organizations has experienced massive change over the five or six decades since the growth of business education, the theories that we use to examine organizations have not experienced the same degree of change.

As guest editor I (somewhat naively) expected to see a series of essays that questioned the original presumption about the need for new theories, or a series of essays that demonstrated how the existing theories have actually modified to keep up with changes in contemporary organizations, and even perhaps (hope-against-hope) some efforts to produce actual new theories.

What we saw however was actually quite different. The bulk of submissions, while very well crafted and interesting, focused largely on the process by which we write theory rather than actually producing new theory. That is, many of the authors attended to the ways in which a literature review produced a gap in knowledge, how to motivate a paper, how to describe constructs clearly, and so on. That is, there was a clear tendency to focus on how to publish theory rather than attending to how existing theory failed to capture changes in the empirical or phenomenal world of organizations. This is a symptom of what I mean by fetishistic theory.

Fetishistic theory has three key attributes. Foremost, it is inherently rational. That is, in the epistemological debate between rationalists and empiricists, fetishistic theory is based on the notion that new knowledge can be derived logically, by parsing texts, rather than by sensory experience. It is also inherently incremental inasmuch as it is dependent on constructing increasingly narrow gaps of knowledge by reinterpreting prior texts. And fetishistic theory is also inherently careerist in that it appears to offer more emphasis on the question of how to persuade reviewers or how to maintain jurisdiction over a research agenda rather than how to construct new knowledge. Ultimately, fetishistic theory leads to fetishism in methods, as Julian observes, and eventually starts to severely constrain what ‘counts’ as authentic empirical experience.

As an editor, I see evidence of fetishistic theory every day in manuscripts plagued with honorific cites, designed to impress and signal rather than to build an argument, tortured posturing to past masters, and undue attention paid to the specific wording of what they might have ‘actually’ said. By engaging in fetishism in building theory we run the risk of becoming priests engaged in the exegesis of scripture rather than scholars engaged in building knowledge and understanding.

Now, to be clear, there are equally important dangers in privileging phenomenal observation over rationalism in building theory. The end result of this error is ‘dustbowl empiricism’, or a complete abdication of theory. Clearly, we need a healthy tension between both approaches to knowledge building.

My core argument, however, is that when we lose this balance between rationalism and empiricism in our approach to theory building, and if we are overly dependent upon theories drawn from outside disciplines, we run the danger of becoming isolated from the phenomenal world of management and organizations. When that happens, the risks of being hijacked are perhaps overshadowed by the bigger risk of becoming irrelevant.

Klaus Weber

I share the perception that the influence of the social sciences – mainly economics, some psychology, and to a lesser extent sociology – is on the increase in the field of management studies. For full disclosure, I happily work in an environment in which over half of my immediate colleagues in my department were trained in social psychology or sociology programmes and more than 80 per cent of my colleagues at the business school are (and see themselves as) economists. But I also spent the formative years of my doctoral education in an environment where the type of scholarship represented by a Karl Weick or Jim March was held in high esteem, and Donald Campbell's fish-scale model of omniscience served as a model for thinking about inter-disciplinarity. (Note that none of these three received their training in management studies!) I have some anxieties – where will our PhD students place in competition with discipline based competition? How committed are my disciplinary colleagues to broad based approaches to management? And I have joy – I learn new things, I enjoy being at the crossroads. So is this trend good or bad? Perhaps ambivalence is (still) the optimal compromise.

I believe that there are certain misconceptions or mis-framings in the debate about management research. One example is the notion that social science disciplines are more specialized and hence their influence leads to a fragmentation of knowledge about management and organizations. Because psychologists are (mainly) interested in individual and group processes, or so it goes, they miss out on formal organizations. And because economists care about markets and formal rationality, they miss out on non-rational and organizational behaviour. Fair enough. But a serious engagement with social science disciplines also offers breadth that goes well beyond their sub-fields concerned with organizations. For example, neo-institutional theory as practised in management departments would benefit tremendously from taking seriously contemporary thinking in the sociology of knowledge, historical political science, and behavioural economics. Perhaps it is management studies that is too specialized, developing theories about phenomena that may be not as unique as they may seem. If organization theory is modelled after industrial bureaucracies, then perhaps it would indeed be more useful to look at organizations as networks, markets, or identities, and compare them to movements, markets, or groups. And is sensemaking, framing, and resource allocation in organizations really that unrelated to similar processes in other settings? At a minimum, there may be a local search problem, where only what is labelled ‘organizational’ or ‘management’ is deemed relevant.

Of course, as management and organizational scholars, we are sometimes miffed that our disciplinary colleagues look down on us as doing ‘applied’ research, when so much disciplinary work is rather applied, too. When one takes policy-oriented economics, large parts of social research in sociology, and professional psychology and contrasts them with more abstract theories of organizations, the division between fundamental and applied starts to look like a serious misconception. If we unpack this sentiment of superiority a bit more, though, it seems to come down more to status and identity threats than to noble concerns about knowledge creation. Management studies are not an identity defining area – how often does one hear people say ‘as an economist, I think …’ or ‘from a sociological perspective …’, and how often, ‘as a management researcher, I think that …’? Perhaps there is a cultural code at work that equates management with the mundane, particular, and pragmatic, and disciplines with the pure, common good, and rigorous. If so, would management researchers more seriously addressing societal goods change that perception? I am somehow doubtful. But it strikes me that we often need our disciplinary counterparts to remind us that organizations are also venues where welfare and wellbeing is produced or undermined.

I remain doubtful because when status and identities are at stake, ignorance follows quickly. The status mobility project of management studies perhaps faces the most serious problem in that researchers in the disciplines do not listen much, creating the impression of a one-way street of knowledge flows. In an ideal world, disciplines – including management studies – would interpenetrate, but it is easy to not pay attention to research that is not produced by the in-group. In this regard, my impression is that disciplines with greater internal heterodoxy (such as sociology, and at some point in time political science), are more open than those with stronger identity defining paradigms (economics, to a lesser degree psychology).

What to do about this state of affairs? Part of the problem is organizational and hard to change: the low representation of management scholars in funding and award agencies, our tendency to speak to the private sector rather than policy makers, the exclusion – in the United States – from liberal arts curricula (many students are rather surprised that one could get a PhD in business), and the separation of business schools from social science divisions in universities. But perhaps if more management researchers were to go outside their comfort zone and try to speak more directly to disciplinary questions, then perhaps management studies would not be as threatened by the influx of discipline trained scholars. If traditional disciplinary boundaries crumble (still a big if), then perhaps trying to be more like a conventional discipline is less important, and being at the crossroads is a healthy identity to be embraced and cautiously cultivated.

Looking Forward

  1. Top of page
  2. Abstract
  3. Editors’ Introduction
  4. Looking Forward
  5. Conclusion
  6. References

Summarizing across your contributions, it seems clear that you all favour an open relationship with other social science disciplines such as economics, psychology, and sociology. There is value, as you all suggest, in an inter- or trans-disciplinary perspective around management phenomena, rather than reaffirming or strengthening strict boundaries between management research and other social science disciplines. The importance of such an approach is perhaps also reaffirmed by the history of management theory which shows that significant advances and frame-breaking contributions were made by management researchers who were free to combine ideas from different disciplines, such as, for example, computer science, biology, economics, psychology, and sociology, and used these ideas in turn to advance our understanding of management and organizations.

Yet, aside from the advantages of a free flow of ideas, this openness may also bring with it the risk that management research becomes infused with generalized versions of discipline-specific theoretical assumptions, formalisms, and technical procedures that are common in other social sciences. Julian mentions the danger of an obsession with technical norms trumping interesting and important research questions. Roy mentions a degree of theory fetishism in our field with theory being imported and reproduced in rather formulaic ways. To be sure, such problems may not primarily stem from the influx of theories and methods from, for example, economics, psychology, or sociology. Yet, it may well be that the very way in which we import ideas and the communities that we erect around them – the one-way street mentioned by Klaus – may reinforce and exacerbate such problems. The risk is one of largely reproducing and mimicking the theories, norms, and methods of other disciplines, but once removed – as we do not directly engage directly in discussions and discipline specific questions in those other areas of the social sciences. Thus, rather than insulating ourselves as management researchers from those other disciplines, one option, it seems, may be to become more comfortable in straddling ideas and methodological approaches from various disciplinary camps, but, as Mark and Klaus suggest, with a distinctive voice and identity. It may be worth exploring this point a little further, and to have a sense of what you see as important ways forward for management researchers and for the discipline at large.

What areas of research, or phenomena, would you consider worth exploring, and how would management researchers be able to bring a distinctive voice or signature to such research? What do you think should we generally do different in our approach to research so that we avoid theory fetishism, technical paranoia, or becoming too insulated and inward-focused? In particular, do you see any areas of research – phenomena or theory – that we have good opportunity to study and learn, but would be susceptible to subversion by some of these concerns?

Julian Birkinshaw

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.

Mark Healey

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.

Roy Suddaby

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.

Klaus Weber

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.

Conclusion

  1. Top of page
  2. Abstract
  3. Editors’ Introduction
  4. Looking Forward
  5. Conclusion
  6. References

As management researchers, we face a promising, yet challenging, future within the social sciences. The debate on these pages suggests that the challenges for the discipline can be addressed if we approach them with the right degree of reflexivity, openness, and level-headedness. The four contributors also identified in turn some paths towards strengthening management studies as an academic discipline that has a direct and relevant impact on managers and organizations. In taking these routes and moving the discipline forward, we may also, as management researchers, be able to carve out a more distinctive and readily recognizable space within the social sciences at large.

Whilst the contributors each make different suggestions, their recommendations seem to coalesce around a common commitment towards management phenomena and towards a kind of research that makes a difference and contributes in a positive way to practice. The focus on management phenomena, first of all, suggests that we have to get our hands dirty and closely observe and study, or even live with, people in organizations – rather than relying on arm's length, or at worst ivory tower, approaches that are based on lab data or proxies. The primary focus on management phenomena also suggests the value of abduction, compared to deduction or induction as the primary canons of scientific reasoning. Julian's example from his own doctoral research and also Mark's suggestions around design interventions suggest an abductive form of reasoning where empirical observations are compared to existing theoretical models and explanations (Alvesson and Kärreman, 2007; Locke et al., 2008), and with such comparisons leading to increasingly more detailed and useful products, whether those are new or revised theories or actual artefacts for practice (Mantere and Ketokivi, 2013). The specific advantage of this type of reasoning for management research is that it requires that researchers are led by observations on the ground, which in turn may help in originating theories with a more distinct management or organizational feel.

A second, but somewhat related commitment shared by all contributors is the importance of making a difference to practice. It is an interesting pledge, and one that historically most management journals, including the Journal of Management Studies, had incorporated as part of their mission statements. Over time, and with the increasing scientific sophistication of our research, this aim came to be seen as a secondary concern for most management researchers and indeed for most management journals. Yet, within our community it may well be an artificial and unhelpful distinction that reinforces a ‘fetishistic’ concern with theory, as opposed to considering how theories, as products, can make a difference and are of instrumental value to managers and others in and around organizations. To tune research in this direction may require that as researchers we push each other to ask bigger and empirically relevant questions, as opposed to being led by the potholes or gaps in a literature. A shift in this direction is also helped by mainstreaming different research approaches and designs, with Julian suggesting a greater use of field experiments, Roy a turn towards ethnographic methods and modes of interrogation from the humanities, Klaus arguing for a focus on empirical settings away from commercial firms, and Mark advocating a design approach based on interventions in practice.

We initiated this debate against the backdrop of the history of management studies and the future prospects for the discipline. Indeed, many of the points and recommendations of our contributors hinge on understanding the recent history of management studies within the social sciences, as a way of identifying the possible roads ahead. Roy in this respect advocates the importance for our discipline of familiarizing ourselves with the historically contingent nature of our knowledge; to foster reflexivity and to better grasp future directions. Such a greater awareness may indeed be much needed, and may help in avoiding the irony of history repeating itself. The pledge for phenomena driven research that makes a difference to practice, whilst highly relevant now, was, for example, already very much a part of the ethos of management researchers and management journals, such as the Journal of Management Studies, in the 1960s and 1970s. Authors who have been highlighted, such as Simon and Mintzberg, wrote groundbreaking articles at the time on a variety of managerial and organizational topics. The leaf that we, perhaps yet again, may take out of their book and with an eye to the future is to ensure that we study managers and organizations across a range of empirical settings up close and are open and reflective in our future research endeavours and not beholden to overly formal and ‘scientistic’ theoretical principles and assumptions from other parts of the social sciences. Instead the great advantage of a phenomenon driven discipline such as management studies is that we, as management researchers, can roam freely for ideas across the social sciences and blend these with an acute understanding of management and organizations. That freedom and creativity is a great gift to scholars and managers interested in a better and deeper understanding of management and organizations.

Note
  1. 1

    Broadly defined here as including both micro and macro research within strategy, HRM, organizational behaviour, entrepreneurship, general management, international business, and organizational theory.

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  3. Editors’ Introduction
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  5. Conclusion
  6. References
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