Back in January, I posted about my thought process in response to a question I had about the Georgia runoff elections. My intention was to illustrate both the crucial role that imagination plays in developing research and ways that imagination combines with analysis to generate myriad hypothetical explanations, each of which could be examined and researched. This post is partly following in those footsteps, but pays more attention to the emotional elements in this process, especially with respect to questions that arise in the process.
As you can see from the title, I’m trying to pack a lot of different ideas in here, but the basic message is that the process of research moves forward by generating a variety of possible avenues of exploration and by choosing one of those avenues. If you recognize that dynamic, you can benefit from it. A crucial part of that approach is the element of confidence needed to make choices in the face of uncertainty. The researcher needs to be able to see a wide array of different possible questions in order to develop a robust argument that can withstand reasonable criticism, but also needs to be able to choose specific limits to each project without any objective logic to determine them. Such limits can be frustrating—they can feel almost arbitrary, or at least arbitrary with respect to purely intellectual issues—but, from a practical perspective, they allow completion. From the perspective of a long-term research practice that wants to produce multiple publications (as expected of professors), these different limits suggest new projects; each acknowledged limit indicates a project that tries to move past that limit.
A “trivial” question
This post was partly triggered by the recent Super Bowl, in which Tom Brady won again. Brady has won the championship an amazing 7 times in 19 seasons, more than 1/3 of the possible titles in those years. According to much of the sports media, Brady is the GOAT (Greatest Of All Time) in football—that he’s the best player ever at the game’s most important position. When I started thinking about that first, I wondered where he stood amongst the wider realm of GOATs: which GOATs are the greatest GOATs? Is Tom Brady greater than Babe Ruth? greater than Serena Williams? It’s a question that could be viewed as trivial: how important is it, really, to identify the GOAT? At the same time, it’s the kind of loose question that could spark research by leading to more detailed questions about how to measure greatness across fields. That question depends on having some idea of how to measure greatness within one field. Which sparks more questions, for example, how do we weigh the peak performance of a player vs. the long-term contribution? How does a player who was really, really great for a relatively short time (Sandy Koufax, Penny Hardaway, Kurt Warner) compare to someone who was just very good for a very long time (Warren Spahn, Jason Kidd, Eli Manning)? And more questions: how do you measure peak greatness? How do you measure long-term greatness? Drilling into any of these questions leads to yet more questions. For the researcher, this can be a bonanza of different potential projects. Or at least could be, if the emotional element is in place: if you tell yourself that a question is trivial, you’re not going to work on it. (I’m not going to be doing significant research on sports GOATs because the questions aren’t sufficiently important to me.) Some questions are trivial, but assuming that a question is trivial too soon can mean ignoring potential courses of research.
Partly this post was sparked was sparked by feedback a writer received on a paper, particularly the phrases “It might have be useful to further discuss…” and “it would have been great to further explore…” Phrases like this are reflections of the process of discovering additional questions: every time we commit ourselves to a new sentence on the page, we offer a target to criticism (but wait…is that true? Every time I commit to a sentence? Are there exceptions?…). Whether or when to answer such questions is largely a negotiation between the author and the audience, taking into account the specific context. It means different things to a student receiving a grade on a paper (that will not be revised) and an author responding to a revise-and-resubmit.
I titled this section “confidence” because the key factor, in a way, is in having the confidence to make decisions of whether and when to pursue these further questions. At any moment in time, there is a limit to what you can do. And in writing, there is almost always a word count limit, sometimes formally stated, sometimes implicit. Therefore, choices must be made: which avenues do you explore and when? Confidence is a necessary guide: without confidence to make your own decisions, you wander aimlessly in response to the most recent stimulus; with confidence, you pursue your own goals and are not swayed by others telling you that your work is trivial. If a question is important to you—if you’re passionate about seeking an answer—that may lead you to ideas that are important.
When I was in college, the whole idea of sports analytics was still relatively obscure. Sports teams didn’t have entire analytics departments; there were no sports analysis websites; there weren’t sports analytics conferences hosted by prestigious universities. Such questions weren’t viewed as particularly important by most involved in sports, and those who didn’t care about sports quite naturally didn’t view those questions as important. Today, of course, sports analytics are a huge industry, and therefore consequential to the many who are involved in sports (though people who don’t think sports are important probably still think that sports analytics aren’t important).
But, when I was in college, sports analytics was just beginning to burst on the scene. The baseball writer Bill James, for example, who started self-publishing his analytics work a few years before I entered college to reach out to a relatively small group of statistical analysts, was starting to gain popularity. James had had the confidence to pursue his work despite the extensive scorn it generated (especially in the early years). James, his colleagues, and those who followed, built sports analytics into a huge industry simply by pursuing questions they found interesting. James would ask simple things like “is batting average the best way to judge a player?” or, more generally, “how do we identify good players?” And he explored those ideas, exploring and developing different analytical methods, revising and refining or even redefining his theories and techniques. He, and the many others who joined that pursuit, simply kept saying “it would be great to further explore…” Indeed, James’s writing often included statements like “when I have time, I want to do a better analysis of X.”
Choosing to pursue a question takes confidence, particularly if others doubt or ask questions. It’s harder to maintain motivation if someone tells you that your work is worthless or uninteresting, and it’s pretty much guaranteed that if you tell enough people about your work, some will find it worthless and uninteresting. It’s not all that uncommon for scholars (particularly graduate students, I think, though I have no empirical evidence) to start to think that their work is so narrowly focused that it is essentially worthless. Questions are inevitable. The question is what to do with them, and confidence is key.
Practically speaking, the scholar faced with a question can do one of three things: they can ignore it; they can pursue it; or they can get bogged down by it. The third can be a big problem. Pursuing questions can take a lot of time and effort. Ignoring questions can actually be good because it allows continued focus on one specific project.
Putting off questions and building a list of projects
When I speak of “ignoring” a question, I don’t necessarily mean entirely ignoring it, but rather temporarily putting it to the side so that it doesn’t derail or delay a current project. Often such a delay can be explicitly acknowledged in writing: every “it would be interesting to explore…” question can be treated with a sort of promissory note by writing “It would be interesting to explore __X__, but that is outside the scope of this project.” Such a response can deflect reasonable concerns by presenting them as the practical choice of a scholar with limited resources (and all scholars have limited resources, especially time): it’s not that you ignored the problem, but that you made the choice to set that concern aside for a time.
From the long-term perspective of a scholar, each of those deferred questions can serve as the seed for a new project. If your system of evaluating football greatness has trouble comparing value across different positions, that’s a project. If your system has trouble comparing across eras (“How do we compare Unitas to Staubach to Montana to Brady when the rules of the game were different?”), that’s a project.
Imagination is a double-edged sword for a researcher: it offers so many questions for further exploration that paralysis can set in. It takes confidence to choose to pursue questions that others view as unimportant, and to set aside questions that others view as important. Still, all questions provide the potential seeds for future projects. Every limit you put on your current project suggests a future project. For someone considering a career as a researcher, it’s valuable to see that dynamic: the question you ask yourself and the questions of others can be viewed as possible future projects rather than flaws in your current work. Every research project has limits or it never gets finished, so it’s crucial to be able to accept questions as limits to the current project even if those questions are obviously important and relevant. I often say that one of the most important phrases for scholarly writing is “but that’s outside the scope of this project,” but at a deeper level, it’s not just about the phrase but about the perspective that it represents. Projects do have limits; it takes confidence to move forward despite limits and doubts. Building a list of future projects from current questions can help build confidence that you are acting responsibly as a scholar or researcher.