From “That’s Interesting” to “That’s Important”
2020; Academy of Management; Volume: 63; Issue: 2 Linguagem: Inglês
10.5465/amj.2020.4002
ISSN1948-0989
Autores Tópico(s)Experimental Behavioral Economics Studies
ResumoAcademy of Management JournalVol. 63, No. 2 From the EditorsFree AccessFrom “That’s Interesting” to “That’s Important”Laszlo TihanyiLaszlo TihanyiTexas A&M University EditorPublished Online:29 Apr 2020https://doi.org/10.5465/amj.2020.4002AboutSectionsPDF/EPUB ToolsDownload CitationsAdd to favoritesTrack Citations ShareShare onFacebookTwitterLinkedInRedditEmail One of the most influential articles in management was written by the late sociologist, Murray S. Davis. The author of several books on humor, human sexuality, and obscenity, Davis wrote an article titled “That’s interesting: Towards a phenomenology of sociology and a sociology of phenomenology” that was published in the journal Philosophy of the Social Sciences in 1971. The article is considered a “cult classic” by many sociologists (Ryan, 2008), and it has also entered the mainstream of management as a required reading in most doctoral programs over the past 50 years.Davis’s (1971) position about theoretical contribution, the focus of Academy of Management Journal (AMJ), is undoubtedly provocative. He argued, “A theorist is considered great, not because his theories are true, but because they are interesting. … In fact, the truth of a theory has very little to do with its impact, for a theory can continue to be found interesting even though its truth is disputed—even refuted!” (Davis, 1971: 309). Based on his examination of sociological theories, Davis offered detailed guidelines in the second part of the article, with the title “The Index of the Interesting,” for the writing of interesting propositions involving 12 logical categories (Davis, 1971: 313–326). The essence of writing interesting propositions, according to Davis, is to demonstrate that “what seems to be X is in reality non-X or what is accepted as X is actually a non-X” (Davis, 1971: 313). Many critics have noted the potential problems associated with the pursuit of interestingness. For instance, Pillutla and Thau (2013) cautioned that emphasizing counterintuitive facts can lead to the development of controversial theories and the collection of unreliable data.Although I share these concerns, my focus in this essay is on the potential trade-offs between writing interesting versus important research. I highlight the need for studying problems that are not merely interesting but are relevant to society and summarize possible reasons for not having it done sufficiently in our field. Important management research can positively influence individuals and groups within and outside organizations, has the potential to improve living conditions in societies, shows ways to build or strengthen ties across nations, or provides findings that consider the interests of future generations. My observations are based on manuscripts submitted to AMJ but highlight a few potential concerns for the field at large.THE PROBLEMS OF FOCUSING ON INTERESTINGNESSWhether AMJ articles are more interesting than articles published in other journals or articles published in AMJ decades ago is difficult to decide. Reading the titles of recent submissions, however, one may conclude that their authors, indeed, are signaling the interestingness of their articles. Catchy titles are not unique to AMJ, but it is possible that similar titles seen in other management journals were the titles of manuscripts previously submitted to AMJ. Theoretical arguments and models in many recent submissions appear to follow Davis’s guidelines for writing interesting propositions rather than substantively advance theories that influence our society or resolve important debates. Access to large data sets has allowed researchers to find small but interesting effects and to model complex interactions and curvilinear relationships when previously familiar associations “flip” or become the opposite. Arguments about less interesting associations have been replaced by bolder statements involving causality, even when such statements are only supported by multiple post hoc analyses. Another sign of emphasizing what is interesting is the limited attention to practical implications. All AMJ articles are expected to discuss the practical implications of their findings, yet this section in many recent articles has been reduced to a short paragraph that often repeats the required theoretical implications in more practical terms. Moreover, practical implications often address short-term profit motives rather than socially responsible management practices with long-term benefits for the broader society.Interestingness is a criterion for publishing in the Journal, as stated in its mission statement: “Authors should strive to produce original, insightful, interesting, important, and theoretically bold research that demonstrates a significant ‘value-added’ contribution to the field’s understanding of an issue or topic” (Academy of Management, n.d.). At the same time, interestingness should not be the only goal for writing for AMJ. As researchers, we are expected to study important managerial and organizational problems. Members of our societies look to us for answers, given our scientific training in conducting rigorous empirical research. Although there might be a “double-edged sword” to everything, our expertise empowers us to do more. It enables us to help our societies in finding answers to a wide range of problems involving management and organizations.For example, it might be true that abusive supervisors are good parents, and a small group of scholars studying leadership could consider this finding interesting. However, it is more important to answer how to respond to or eliminate workplace abuse. There are also many studies on how managers engage in impression management, but relatively fewer studies focus on the organizational and individual implications of dishonest communication. Similarly, some might find it interesting that state-owned enterprises can be competitive and profitable. However, studies trying to explore the interesting sides of these organizations tend to discount their macroeconomic costs and ignore the century-long conclusions in economics about their poor performance and lack of innovation. Alternatively, studies could investigate the benefits of privatizing them or identify certain conditions under which they can provide value.There are methodological implications of focusing on what is interesting. On the one hand, those who study important societal problems may be vulnerable to the same biases and errors as those who highlight interesting results. Indeed, authors can falsify their data or p-hack their results because of self-interest or in order to influence societal conversations. On the other hand, the process of trying to engage attention by discovering counterintuitive relationships can easily lead to hypothesizing after the results are known, or “HARKing” (Kerr, 1998). One could make a case that the ease of data access and the advances in analytical tools in recent years have increasingly allowed researchers to discover unusual findings at the cost of testing theories on meaningful relationships. The quest for interestingness has resulted in findings that appear only under unique conditions and the construction of complex statistical models that could fall apart in subsequent replication efforts.WRITING IMPORTANT MANAGEMENT RESEARCHScholars concerned about the theoretical or methodological state of the field have been advocating for problem-driven research (Davis & Marquis, 2005; Pillutla & Thau, 2013). Problem-driven research is suitable for studying organizational problems with strong societal relevance, but studying important research questions does not require a sacrifice in terms of theoretical contributions. New theories on management and organizations are not developed in isolation. For instance, many theories have emerged with the aim of explaining and providing solutions to societal problems and crises (Perrow, 1973). However, such responses by theorists have been slower in recent years. Most major theories we use in our field were written more than 40 years ago. Ten years after the Great Recession, it is time to develop theories that help improve managerial behavior and organizational actions that make similar devastating societal crises easier to overcome or to avoid.Ferraro, Pfeffer, and Sutton (2005) reminded us that developing new theories to address new problems is important because theories can become self-fulfilling. Our theories and findings, via the pages of textbooks, teaching, and through the media, can shape the minds of future managers. While we can earn high marks in the classroom by discussing our counterintuitive empirical findings, we have a long-term commitment to teaching managers how to lead their organizations ethically and how to serve their stakeholders and communities.Several factors have encouraged management scholars to focus almost exclusively on what is interesting. To increase our attention to societal problems involving management and organizations, many of those factors need to change. Scholars in business schools tend to have better access to resources required for empirical research. Unlike their counterparts in liberal arts and natural sciences, most management scholars do not need to justify the purpose of spending of research funds to government agencies. Furthermore, subscriptions to large databases and access to undergraduate students or paid professional survey respondents, like the individuals on MTurk, provide quick and inexpensive access for the testing of interesting ideas. In contrast, studying controversial organizational problems requires substantial financial investments, takes a long time, faces bureaucratic barriers, and carries substantial risks of failure.To recognize and reward important research, the way research productivity is evaluated in management will need to change. The current system used by many schools encourages multiple publications regardless of their topics or the importance of their purported contributions. Moreover, the impact factors used in the field do not measure an article’s societal impact. When they are cited by peers, articles with surprising findings may be favored over articles with relevant findings. The media, especially the online media, further encourages the production of attention-grabbing findings. Lastly, more patience is needed when we evaluate submissions for and read articles in AMJ. Instead of looking for studies with surprising findings or from rare empirical settings only, we need to encourage work that investigates important managerial and organizational problems. To facilitate this effort, the editorial team of AMJ has issued a call for papers for a new Special Research Forum (SRF): Joining Conversations in the Society on Management and Organizations. Further details on the SRF can be found in this issue.CLOSING COMMENTSBy following Davis’s (1971) proposed logic for writing interesting articles, one can state two propositions involving a social problem:What seems to be a solvable societal problem is in reality an unsolvable problem.What seems to be an unsolvable societal problem is in reality a solvable problem.Although some may find the answers to both propositions interesting, the second proposition—discovering solutions to real problems—will move societies forward. How can corporate innovations improve or save lives? Under what conditions might countries and people benefit from international trade? How can mangers improve working conditions for their employees? How can organizations become more inclusive? Can businesses and governments work together effectively to solve societal problems and crises? As scholars, we are expected to seek solutions with our research to these and other difficult questions involving management and organizations.Finally, with regard to this particular essay, I would like to thank Katherine DeCelles, Luis Diestre, Denis Grégoire, Ivona Hideg, Jennifer Howard-Grenville, Bart de Jong, Cindy Muir (Zapata), Andrew Nelson, Floor Rink, Matthew Semadeni, Jason Shaw, Elizabeth Umphress, and Gurneeta Vasudeva for their helpful comments.REFERENCESAcademy of Management. n.d. Mission statement. In Welcome to AMJ [Web page]. Retrieved from http://aom.org/Publications/AMJ/Welcome-to-AMJ.aspx. Google ScholarDavis, M. S. 1971. That’s interesting!: Towards a phenomenology of sociology and a sociology of phenomenology. Philosophy of the Social Sciences, 1: 309–344. Google ScholarDavis, G. F., & Marquis, C. 2005. Prospects for organization theory in the early twenty-first century: Institutional fields and mechanisms. Organization Science, 16: 332–343. Google ScholarFerraro, F., Pfeffer, J., & Sutton, R. I. 2005. Economics language and assumptions: How theories can become self-fulfilling. Academy of Management Review, 30: 8–24.Link , Google ScholarKerr, N. L. 1998. HARKing: Hypothesizing after the results are known. Personality and Social Psychology Review, 2: 196–217. Google ScholarPerrow, C. 1973. The short and glorious history of organizational theory. Organizational Dynamics, 2: 3–15. Google ScholarPillutla, M. M., & Thau, S. 2013. Organizational sciences’ obsession with “that’s interesting!” Consequences and an alternative. Organizational Psychology Review, 3: 187–194. Google ScholarRyan, D. 2008. Murray S. Davis 1940–2007. Footnotes, 36: 14–15. Retrieved from https://www.asanet.org/sites/default/files/fn_2008_07.pdf. Google ScholarFiguresReferencesRelatedDetailsCited ByWhen Tax-Exempt Nonprofits Detract Value from SocietyEdward N. 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