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Biggart's Lament, or Getting Out of the Theory Cave

2016; Wiley; Volume: 53; Issue: 8 Linguagem: Inglês

10.1111/joms.12185

1467-6486

Nicole Woolsey Biggart,

Information Systems Theories and Implementation

In this essay I lament what I see as the unrealized potential for organization studies to contribute to society by considering more explicitly issues of public concern. I suggest how we can begin to move in that direction, if we want to. Disciplinary Science Engaged Research Impact Science Problem-Oriented Research Theory Like many of you I came to the study of organizations because of experiences that intrigued me and about which I wanted to learn more. In my case I had improbably landed an internship job with the Postmaster General of the USA just as the postal service was trying to transition from being a cabinet-level and therefore highly politicized unit of the Executive Branch to an enterprise-like public corporation. Republican President Richard Nixon was trying to reduce political patronage and the cosy relationships between largely Democratic postal unions and Congress. Nixon also wanted to improve efficiency and run the mail system in a business-like way (modernizing government was a theme of his presidency). At that time the post office was huge – the largest non-military organization in the world with thousands of employees in nearly every community in the country. It owned more real estate than any other organization. It had fleets of trucks, bought vast petroleum supplies (as well massive amounts of products from paint to paper), and had large contracts to move mail with airlines, railroads, and trucking firms. It had millions of dollars of receipts coming in every day, an extraordinary cash flow the management of which was… unsophisticated. Organizationally it was not just large, but complex, and riddled with traditional ways of doing things, some probably traceable to the first Postmaster General, Benjamin Franklin. Moving the behemoth towards modern logistics and customer service was to be an extraordinary process, if possible at all given multiple entrenched political interests. It was a fascinating time and place to be and I had a fine perch in Washington DC from which to observe. The management internship programme I was in moved me around to different functional areas but I was always tied to the Postmaster General's Office and had a view from the top, essentially corporate headquarters. I did everything from assessing whether building maintenance workers could be trained to fix new optical character readers, to helping to develop Express Mail (the first new product since World War I and the development of aviation), to writing articles about mail being carried by mule in Kentucky and by boat up the Detroit River. I ran two post offices and merchandised philatelic products. I negotiated a labour contract. After I had experienced the power of organization to shape material processes and workers' lives I wanted to learn more so that I could do more. I was perhaps naive but I thought that I could be a force for good in public administration or business. Graduate school gave theoretical structure to what had been my professional life. I had essentially no intellectual training for organization studies but I did have more experience in organizations than most of my fellow students. Most of them had to do fieldwork in order to have something to write about; I had to read theory in order to write. I loved theory! It helped me to understand what I had experienced, gave me a way of looking and thinking and making sense of the world. It was so useful. As a graduate student I wrote about organizational change in the post office, and thanks to Watergate about scandals in the White House. I figured out why US presidents and Cabinet officers had large patrimonial staffs such as the White House staff and the one I served in, very unlike Europe's heads of government who rely on ministries to do their work. Early on I was very influenced by my reading of Weber whose descriptions of bureaucracy and patrimonial administration coincided closely with my observations of life in Washington. I loved Weber but other perspectives and writers were eye opening too. Many of my favourites were veiled calls to action and certainly stirred public discussion of our organizational society. I liked scholarly works with a critical and theoretical perspective, but readable too, works that would inspire comment and even action. My favourites included Selznick's pragmatist work TVA and the Grass Roots about a socialist project in the rural US, Mills' mixing of Weber and Marx in The Power Elite, and Bendix's superb Weberian study of managerial ideology in Work and Authority in Industry. It inspired my own paper on theories of success in popular business literature. Who didn't love The Organization Man, which helped me to understand the working fathers I had grown up near in a New York City suburb? Arlie Hochschild was working on what would become another favourite, The Managed Heart about emotional labour in our increasingly service-based economy. Often non-academic audiences read them too. They were impactful. Whatever my expectations had been about publishing in a management school setting at a research-intensive university, they were not supported by my realization that I needed to double-down on theory and generate novel theoretical insights, not just use theory, but make theory. Novelty trumped impact in order to get noticed. Frankly I loved immersion into a theory-rich world that was intellectually challenging. The impulse I had once had to be useful to a world of organizations was however, if not gone, very much buried in conference papers, revise/resubmits, relationships with colleagues, and the need to figure out what I could write for the next special issue recently announced. I became what was valued in my professional community: a scholar who wrote about those things that were 'sellable' and sufficiently abstract to avoid the accusation of 'applied'. That earlier impulse – quietly buried – to have impact on a broader society has reawakened for several reasons. As a senior scholar I feel freer to do something outside the usual channels. And while I continue to enjoy constructing yet another publishable and hopefully smart thesis at the intersection of pragmatist theory and the French conventions school (Beamish and Biggart, forthcoming) the frisson is no longer the same. But mostly my unease at being an arms-length and often-irrelevant observer developed when I assumed administrative posts. For 11 years I was in regular contact with people who struggled to find solutions to very real problems. Six years as dean of my management school and five more as Director of the UC Davis Energy Efficiency Center (EEC) revealed a yawning gap between what I wrote and real issues facing organizations, their leaders, and society. It's hard to go back to a theory cave after that. My personal experience reflects the decades-long transformation of business schools in the USA that Rakesh Khurana wrote about in From Higher Aims to Hired Hands: The Social Transformation of American Business Schools and the Unfulfilled Promise of Management as a Profession. Law schools and medical schools developed by teaching mastery of knowledge and the application of that knowledge to do good within the framework of professional ethics. Business schools started on the same track as medical and law schools but changed course. B-schools transformed from aspiring professional schools as sites for the teaching of skills and practice within an ethical frame to something akin to social science departments as practiced in disciplines such as psychology, sociology and economics. When we reproduce disciplinary departments we give up our ability to engage in scholarship that has clear connections to organizing and practice. I am not suggesting that we become organizational clinicians, rather that we create concepts, ideas, and possibilities that engage the issues of the day – the loss of middle management, the impact of gender imbalances on corporate decision-making and how new forms of expertise and authority emerge in the economy. Directing the Energy Efficiency Center was an intellectual and management stretch for me. The EEC is a cluster of applied research units, mostly based on engineering solutions to energy sustainability problems such as the colour rendering of low-energy LED light bulbs to make them more appealing to consumers and spur adoption, and figuring out how much energy it takes to produce the clean water that we consume in my state – 20 per cent of all of California's electricity goes to moving and cleaning water. Changing policy around the 'water-energy nexus' is a major effort at the EEC and involves more than a little data collection and analysis and inter-agency diplomacy to say the least. (To see more about the EEC's work view http://eec.ucdavis.edu and the centres it supports). The EEC is highly regarded by industry and government as a politically disinterested territory for developing good ideas and technologies to help the environment and the public good. We had no driving interest other than in saving energy and carbon and had financial support from multiple organizations in different sectors. After a couple of years I mostly could understand the industry and governmental, regulatory and NGO actors and the interests involved. I realized that while many of the 'solutions' industries pursued might have made good engineering sense, they made little sense from a management or social science perspective. Houses are not just physical boxes with differing thermal mass, but homes with social, cultural and historical meaning embedded in neighbourhoods. Retailers don't just want to save money on lighting, they want their goods to look attractive while displayed. People don't just buy cars for their efficiency characteristics, but for status and aesthetic reasons too. Some good technologies won't work because they are incompatible with previous technologies. Do sensors on electricity meters really manage home electricity use or are they there to spy on people and emit brain-altering waves, as one tightly knit Northern California community decided? Some solutions work, or fail to, because of network effects, or peer pressure, or economic structure. How do you push the oligopolistic industrial cooling industry to improve products when it controls the market? I could go on, but the point is that many if not most of the issues that the EEC deals with are industry structure and socio-technical problems. Society is in the technologies and technologies must live in society. The fact is social scientists are welcome, even desired participants in these sorts of efforts because engineers are problem solvers and they want things to work. They are happy to have a little chemistry, some physics, and a touch of management thinking to develop good solutions. As Director of the EEC I was invited to give the closing keynote lecture to a conference held in 2011 by the Engineering Directorate of the US National Science Foundation in Washington DC. The conferees were examining technologies in anticipation of nearly US $1 billion of sustainability funding. I started my talk by discussing three technologies (slides pulled from my technology management class) that were engineering successes but failed miserably. One failed for political reasons, one for the cultural obtuseness of the technologists, and one because it did not take into account existing institutional arrangements. The response was as expected – surprise. They thought that engineers developed the solutions and social scientists sold them to the public. I said that if social science isn't there at the beginning, it's likely too late. Recently I gave a keynote at the Low Carbon Living Collaborative Research Centre in Sydney, Australia. I followed a panel of business executives who were befuddled by so many smart professors and PhD students who could not engage with them because there was a fundamental disconnect between what market relations demanded of business and the academics' purposes. Everyone wanted to reduce carbon in the economy but there was small-to-no common place for collaboration – different focuses, different schedules for action, and no shared stake in engagement success. These are solvable structural and organizational barriers. So it's not that we aren't welcome in important research areas where organizational issues are central and that many of us find interesting. Many of the problems that face global societies are organizing problems, problems that deal with systems, interfaces, culture, networks, institutions, and motivations in all their complexity – exactly the issues that need elucidation. I keep hearing people say we need a concerted push to deal with climate change, something like a Manhattan Project or moonshot programme, but that won't happen for carbon reduction or most other complex problems the world faces. There are too many existing technologies, interests, and institutions in place to have one concerted effort. I know of no group more intellectually capable of looking at these issues and possibilities than my organization studies colleagues in management schools. If theory-centric novelty is the purview of top management journals and top journals do not measure social impact other than citations in Google Scholar then we will not be encouraging work that has meaning outside of our small professional circle. I do believe that there is an opening for more engaged and impactful studies by organizational scholars, however. One of the things I learned as a dean working with other deans was that many fields, particularly the natural sciences, have shifted from a discipline-only-basic-science approach to discovery, toward problem-oriented and interdisciplinary work. Climate change and sustainability research now routinely includes teams of atmospheric and soil scientists, biological systems analysts, ocean physicists, and many more research areas. Public health researchers include everything from biostatisticians and toxicologists, to entomologists and social network theorists. This shift has not come easily for disciplinary science on my campus and is taking years to mature. Research partnerships that try to surmount the knowing-doing gap, varied funding sources and even authorship concerns are not trivial issues for a post-normal science world but they are being addressed. Fundamental issues such as who defines the questions and problems, what data and methods are to be used, and how the discoveries can be connected to policy and solutions are part of the challenge. What are the bases for evaluation by reviewers? What new governance structures are needed to guide the research? Assessing quality and impact demands new criteria and new understandings of research 'success'. Despite growing pains impact science is here to stay and there is increasing pressure for it in research-intensive universities. The public, whose support is a critical source of grant income in many places, is demanding that university researchers become part of the solution to the grand challenges facing societies. In the most recent Research Excellence Framework (REF), a nationwide assessment of higher education institutions conducted every few years in the UK, a new criterion was added – Impact. Universities vying for high scores that mean both prestige and enhanced funding had to demonstrate through cases – not citations – how their research is having impact on the wider society. In the 2014 REF there were 6975 cases submitted for evaluation and are available for view on a database. Over 80 per cent of the cases included two or more 'field of research' codes, suggesting the importance of multiple disciplines for the examination of problems. Clearly there is a great deal of public-spirited research happening in the UK and there is now institutional pressure that will support this sort of work. In the USA the Carnegie Foundation is an important source of university classification into categories such as Baccalaureate Colleges, Master's Colleges and Universities, and Doctorate-granting Universities that are further parsed into research institutions of various intensity. Each is not just a categorical distinction but also a status marker. In 2005 a new voluntary classification scheme was introduced, the Community Engagement Classification. This classification involves certification of the mutually beneficial exchange of knowledge and resources by an institution and its larger community, which can be defined as anything from the local community to global society. 'Engaged' institutions by definition are doing more than disciplinary and abstract theory work, but rather are sharing information and in some instances collaborating in 'citizen science' projects by involving community partners in research of mutual interest. The 2015 list of Carnegie Community Engaged Institutions includes 240 schools many of which are research-intensive. If you can be persuaded that there are important social problems that invite organizational analysis, and that there are growing forces that might support our engagement in problem-oriented research, what can we and what should we do as organizational scholars mostly in business schools? First, let me say that I am not suggesting a trade-off between theory-focused and problem-focused research, but rather that more organizational scholarship take a greater public good orientation. I am also not suggesting that we become consultants but rather take up more research that is directly connected to the many obvious issues that face our global economy and society. I am arguing for an intellectual space that we build somewhere between consultancy (where one gets paid to solve a problem that has been defined by a client) and speaking only to one's erudite peers (preferably in a precious language that only the right people will understand). Clearly there are some of us already doing this sort of work but the legitimacy that comes with prestigious funding sources, publications in respected journals, and recognizable career rungs are hardly in place. But these are organizational problems that we can solve, if we want to. First, I don't think there is a funding issue at all. In fact if we are willing to partner with other disciplines that depend on problem-oriented research we will have access to new research riches, ideas and relations. I am asked all the time if I am available because I have gotten outside the management school. The problem is getting up and meeting people and letting them know that you are willing and able to participate. That's not a small barrier because at least in the USA B-schools tend to isolate themselves from the main campus. However, jumping barriers is good intellectual exercise. There are multiple ways to start. Would this pass the legitimacy test for people worried about their careers? It depends. It will take the right people, the right universities and research institutions, and the right journals to support these efforts, and it will take time. But given the signs that there is interest in truly impactful social research maybe this is the right time. For those of us who have made a career out of interpreting the footnotes in Capital remember that Marx was an activist and journalist as well as a theorist of the highest order. He could mix it up with material reality. Weber worked as a hospital administrator during World War I, and was a political pamphleteer and essayist (remember 'Politics as a Vocation' and 'Science as a Vocation'?). I happen to agree with a favourite activist of mine, Gloria Steinem, who said, 'Feminist theory came from feminist activism – it wasn't the other way around'. Maybe we will become better theorists by leaving our theory caves and using our ideas and abilities to help solve a world of organizational problems. I say, let's find out.