Choose Courage and Swing for the Fences

My good friend Jim Detert recently published a great book called Choosing Courage: The Everyday Guide to Being Brave at Work. Among other topics, he talks about what courage in the workplace looks like, why people so often fail to demonstrate it when the opportunity arises, the rewards (and sometimes costs) of taking courageous acts, and picking your battles. In addition to its applicability in our everyday academic lives working in our departments and universities, I also see its applicability to academic writing. In this blog post I focus specifically on how choosing courage applies to the topics we study. Some may ask, it takes courage to choose a research topic? My answer is a resounding yes. As Jim discusses, courage is behavioral and perceptual; it’s you engaging in behaviors that others perceive as risky.

Too often I see and hear about junior scholars choosing “safe” topics because they are popular or they think the studies will be easier to conduct, not because they are interested in the topic. They rationalize that they will take on bigger, riskier topics once they have tenure. However, ample work on intrinsic and extrinsic motivation has shown that if you study something because you think it’s safe or popular (i.e., for extrinsic motivations), rather than because you’re intrinsically interested in it, the work is going to be less creative and you will be less likely to persist in pushing it forward if you run into difficulties. This work is thus less likely to end up in top-tier journals or be highly cited. Further, by the time folks pursuing safe, extrinsically motivated topics gain tenure their research die is cast. They are unlikely to change their approach to research, and continue focusing on incremental topics that are more likely to be overlooked, have limited influence on the field, and are more likely to be published in lower-quality journals or little-read book chapters.

So what makes a topic risky? Topics that others are not currently studying can be risky for a variety of reasons. There may be little literature to build on, there aren’t current conversations to join, it may be difficult to find knowledgeable reviewers who can evaluate your work or see its importance during the review process, and if no one else is working on the topic, then there won’t be anyone to cite it. On the other hand, if you end up spawning a new theory or topic domain, or you catch the wave and are one of the first papers published on a topic that lots of others are also starting to pursue, then the study could be a career-making work.

A number of years ago Ken Smith and Mike Hitt published a book called Great Minds in Management, where macro and micro scholars who developed some of the most influential theories in our field (e.g., Al Bandura, Jay Barney, Richard Hackman and Greg Oldham, Don Hambrick, Ed Locke and Gary Latham, Jeff Pfeffer, Karl Weick, Oliver Williamson) told the stories of how their theories came about. The stories are fascinating; some faced strong headwinds in getting their work published, others caught or started a wave, and some backed into their big ideas accidentally, or through serendipity. But all of them took risks in developing novel ideas, creating new research domains and challenging the status quo.

Topics can also be risky when they involve a controversial or stigmatized context or set of ideas. The scholars risk being tainted by the stigma of their research subjects. For example, when my former student Kisha Lashley was thinking about studying the medical marijuana industry for her dissertation, at least one faculty member warned her not to because it was too “risky” a topic. Luckily she didn’t listen. I was very supportive of the topic, although I told her there was some chance she could become known as “the pot lady” if the study wasn’t theoretically rigorous (it was). And there were indeed a couple schools that didn’t want to interview her because of her dissertation topic. However, many more schools and scholars found her topic and dissertation intriguing; she landed a great job, the paper based on her dissertation was published in Administrative Science Quarterly last year, there are dozens of other scholars who are now pursuing research in this context, putting her at the leading edge of a hot topic, and she’s becoming well-known in her field.

Finally, topics can be risky because the data is hard to get, or the topic employs an unconventional research design or presentation structure. If your data collection is ultimately unsuccessful, then you have wasted lots of time, and possibly money. And if the resulting story requires an unconventional format to be effectively told, it can be harder to get through the review process. Mixed-method studies are a classic example. When I was an AMJ associate editor I handled one paper that had an interesting premise, a context I loved (high-end restaurants) and involved both a field experiment and qualitative research, but the initial submission tried to force the story into a more conventional format, and it didn’t work. I gave the authors a revise and resubmit, and encouraged them to follow a more unconventional format that allowed them to make fuller use of their mixed-method data and tell the story in a more engaging way. This was a risky decision for them; the lead author was untenured at the time, and there were few studies (specifically only one that I knew of, and pointed them towards) that employed this format. However they took my suggestion, and indeed one of the reviewers reacted very negatively. They did a good job executing the study, though, the other two reviewers and I were supportive, and I ultimately accepted the paper. I have seen another, similar situation, however, where the editor suggested some untenured authors pursue an unconventional structure, they followed the editor’s recommendation, the reviewers reacted negatively, and the editor didn’t back them, rejecting the revision. So, it can go both ways. That’s why it’s risky.

There’s a reason why the top home run hitters in baseball also often have the most strikeouts; they take big risks and always swing for the fences. Not every successful or important study is on a high-risk topic, but at the times they were done, many were. If you have the courage to pursue topics you find intrinsically interesting, put in the hard work and persist, and learn from your setbacks and failures, you are more likely to have few regrets, and to have the kind of career you hope for.