What Don’t We Know, and So What?

I was the PhD coordinator for nine of the fourteen years I was at Penn State. Working with doctoral students and helping them launch their careers is the most gratifying part of my job. It’s always great to see former students achieve success. I recently read two excellent articles by three former PSU doctoral students who have gone on to successful careers—Joel Gehman, Abhinav Gupta and Chad Murphy.

Joel is now a full professor at the University of Alberta, and Abhinav and Chad are Associate Professors at the University of Washington-Seattle and Oregon State University, respectively.  Joel’s article, coauthored with Jean-Francois Soublière, titled “The legitimacy threshold revisited: How prior successes and failures spill over to other endeavors on Kickstarter” was published in Academy of Management Journal in 2020. Abhinav and Chad’s article, coauthored with Anna Fung, titled “Out of character, CEO political ideology, peer influence, and adoption of CSR executive position by Fortune 500 firms,” was published in Strategic Management Journal last month. These studies provide excellent examples of two different ways you can problematize existing research and identify your theoretical contribution.

Karen Locke and Karen Golden-Biddle identified problematizing, along with “establishing the intertextual field” (i.e., identifying the conversation you are joining), as the two processes involved in answering the questions, what do we know, what don’t we know, and so what? Problematizing addresses the last two questions: establishing what we don’t know, and why it’s important. They identified three different approaches to problematizing: incompleteness, inadequacy and incommensurability.

Abhinav, Anna and Chad’s paper illustrates the incompleteness problematization. They argued that whereas substantial research has explored how peer firms’ actions affected a focal firm’s decisions, “Curiously, however, prior inter-organizational imitation research has largely overlooked how the characteristics of the decision-makers in these referent firms—that is, the CEOs who are highly visible to observers—might influence the likelihood that their firms' decisions will be emulated”. This relative lack of attention to executive characteristics is problematic, particularly when viewed through the lens of upper echelons theory, which suggests that CEO personal characteristics, such as demographic attributes, occupational background, personality, and values, fundamentally influence firms' decisions.” They theorized that when faced with a decision which was at odds with their own political ideology, a focal CEO would look to other CEOs who shared their ideology and faced the same incongruent decision, and would be more influenced by these CEOs’ actions. Specifically, they focused on the decision to add a corporate social responsibility (CSR) executive to their top management team. They found that when more politically conservative CEOs saw other politically conservative CEOs add CSR executives, the focal CEO was more likely to do so, as well. They argued the incongruence of the situation made the decision, and the other CEOs’ behaviors more salient, and influenced whether they attributed the motivations underlying the decision to situational versus dispositional factors. Adoptions by peer firms with politically liberal CEOs didn’t have the same effect because they didn’t perceive this as an incongruent decision for them. They also found these effects were enhanced when shareholders were directly pressuring the focal CEO to add a senior CSR executive. Thus, they didn’t argue that prior research about peer influences on decision making was wrong; rather, it was incomplete because it hadn’t considered the dispositional characteristics of the CEOs, rather than the more typical firm-level similarities. They answered the “what don’t we know?” and “so what?” questions by changing the focus to a different level of analysis and showing how perceived similarities and differences in peer executives’ values shape peers’ influences on decision making.

Jean-Francois and Joel’s paper is a good example of the incommensurability problematization. They argued that while a substantial amount of research has explored the importance of legitimacy for entrepreneurial startups, and scholars have also theorized about how the actions of similar others can enhance a focal firm’s legitimacy, little research has explored how this actually occurs. Further, legitimacy has essentially been treated as binary: once you surpass some threshold you have it, and if you don’t surpass that threshold, you don’t have it. Joel and Jean-Francois made novel use of the crowdfunding context on Kickstarter to argue the existing conversation was incommensurable because, they didn’t just say it was inadequate, but that it was wrong because it is based on two faulty assumptions. First, they argued that the legitimacy spillover effects of others’ successes and failures weren’t binary; rather the magnitude of their successes and failures mattered. Second, they argued that both successes and failures can enhance and retard legitimacy spillovers to others. As such, “The dominant wisdom does not easily apply to novel contexts such as crowdfunding.” Combining these two insights, they theorized that whereas “blockbuster successes”—which far exceed the legitimacy threshold—enhance legitimacy, “unsung successes,” which barely exceed the legitimacy threshold have negative legitimacy spillover effects. Further, they theorized “pathbreaking failures” which come close to succeeding, and bring new interest in and investors to an area, can also result in positive legitimacy spillovers, whereas “broken path” failures that don’t come close to crossing the legitimacy threshold have negative spillover effects. Thus, by challenging two assumptions in the existing literature as wrong, and what happens when you relax these assumptions, they showed us what we don’t know, and why it’s important.

These two examples illustrate two different ways to problematize research, highlighting the interesting and important theoretical contributions your studies make. I hope that explicitly considering these examples helps you see new opportunities for developing interesting and novel contributions in your own work.

Note: I’ve updated this blog post. In reading Jean-Francois and Joel’s paper, I’ve revised my thinking and now see this as an example of an incommensurability problematization because they are saying two assumptions underlying prior research are wrong. So, while there is some judgement involved in categorizing problematization approaches, the point is that they effectively problematized the prior literature to show what we’d learn and why it’s important.