How Do You Choose a Good Research Topic?

Everyone’s been there.¹ Maybe you’re looking at a class assignment. Or maybe it’s the next conference paper or journal article. Or maybe it’s a larger-scale thesis, dissertation, or book project.

You have a sense of who you want your work to address. But you’re having trouble coming up with exactly what you want to discuss.

There isn’t a magic formula for invention, or finding a good research topic. But it’s helpful to frame that search in terms of the importance of imagination and the hermeneutic priority of questions.

Imagination and the Hermeneutic Priority of Questions

H.-G. Gadamer reflects,

Imagination … is the decisive function of the scholar. Imagination naturally has a hermeneutical function and serves the sense for what is questionable. It serves the ability to expose real, productive questions….

As a student of Plato, I particularly love scenes in which Socrates gets into a dispute with the Sophist virtuosi and drives them to despair by his questions. Eventually they can endure his questions no longer and claim for themselves the apparently preferable role of the questioner. And what happens? They can think of nothing at all to ask. Nothing at all occurs to them that is worth while going into and trying to answer.

I draw the following inference from this observation. The real power of hermeneutical consciousness is our ability to see what is questionable.²

The ability to “see what is questionable” helps us to “break the spell of our own fore-meanings.”³ That is, it puts us in a state of openness to understand the realities we encounter in different ways than we do at first blush.

Good research answers a question. And a key step toward answering a question is “seeing what is questionable” so that you can ask the question.

You might not ask the question as such in your project. But the question you’re answering needs to undergird the whole project. That way, your project will have coherence as an answer to that question.

Two Kinds of Questions

The questions you can ask are as infinite as the possible combinations of material involved in biblical studies. For all that breadth, though, the questions basically fall into two types.

Good research projects try to answer questions that are either

1. known as such or based on known themes or
2. unknown at all, or at least unknown as live questions.⁴

Questions Known as Such or Based on Known Themes

An example of a known question would be “What is the nature of verbal aspect in Koine Greek?” Similarly, once someone tried to answer the question “How does Paul use Isaiah in Romans?” the question “How does Paul use Isaiah in 1–2 Corinthians?” became a known permutation of the same theme.

Questions Unknown or Unknown as Such

You can also base research on a question that’s unknown, or at least unknown as a live question. Doing so requires you to interrogate the basic assumptions undergirding a topic. The struggle to frame unknown questions often includes activities like “a willingness to try anything, the expression of explicit discontent, the recourse to philosophy and to debate over fundamentals.”⁵

For instance, by the late 1970s, the discipline of “Old Testament introduction” was well established. Writers of introductions to the Old Testament followed predictable patterns. One of those frequent patterns was treating the topic of an Old Testament canon only at the end of the introduction, or not at all. Canon wasn’t central to the discipline. And that judgment was the accepted status quo.

In his Introduction to the Old Testament as Scripture, however, Brevard Childs argued that this very assumption wasn’t well founded.⁶ Canon wasn’t a subsidiary crater in the wider topic of Old Testament introduction. Still less was it some other topic in another field outside Old Testament introduction. Rather, the question of canon was actually part and parcel to the whole field.

Questioning the assumed irrelevance of canon allowed Childs to open a new line of questioning. That line then became a known kind of question. And scholars began asking, in varying ways, “What might it do for Old Testament interpretation if these texts were approached as canonical literature?”

When Will a Question Lead Somewhere Interesting?

Of course, not all questions that can be asked are good to ask. Simply because you have a “willingness to try [or ask] anything” doesn’t mean just any question will lead anywhere interesting.

Gadamer’s Reflections on the Sophists

Gadamer’s description of Socrates’s interaction with the Sophists is again pertinent. Socrates’s interrogation ends in the Sophists’ exasperation—their “expression of explicit discontent.”⁷ They then “claim for themselves the apparently preferable role of the questioner.”⁸

But inevitably, the Sophists’ questions either don’t materialize, or if they do, they go nowhere. As Gadamer summarizes, “Nothing at all occurs to them that is worth while going into and trying to answer.”⁹

This situation shows how not all questions, when formed, prove productive. Perhaps no question is “bad” in itself. But that doesn’t mean that all questions are “good” for the purpose of driving a research project.

Good research must have a point. It must go somewhere. But as in the case of the Sophists, not all questions one might ask are “worth while going into and trying to answer.”¹⁰

All this raises the question of how you can identify a research question that will lead somewhere interesting. Sometimes, you might come across a question that you might feel sure about in this respect. When you do, that’s great.

But how do you test that assumption? Or if you’re more ambivalent about whether your question will go somewhere or not, how do you decide?

To this concern there are basically two answers. Namely, you can expect a research question to lead somewhere interesting if

1. you can show why your question addresses a problem,
2. you can keep asking more questions based on your initial question, or
3. both.

Show Why Your Question Addresses a Problem

In this first case, your question falls in the category of questions unknown, or at least unknown as live questions. For such questions, it’s your job to show your audience why they should share your question.

Helping your audience share your question might mean you get to say nothing, or only very little, about where you think the question leads. If your question needs to unseat something “everyone knows,” it might take quite a lot just to show why your question is worth asking.

To start grappling with this task, you might ask yourself other questions like:

• What problems are there inside what “everyone knows” that get glossed over?
• On the basis of what “everyone knows,” what next steps is it difficult to take?
• On the basis of what “everyone knows,” what other questions is it hard to answer?¹¹

Keep Asking More Questions

Of course, any specific research question might actually not go anywhere. Like the Sophists, you might see only a dead end. Or you might only find that the end of a given question isn’t terribly interesting. If so, it won’t be a question you’re able to help your audience share.

On the other hand, as with Socrates, good questions beget more good questions. Framing a topic well at the start helps you and others see any number of new trails start to open up as you contemplate exploring that topic further. So, the ability of a question to keep the discussion going is also a good indicator of the question’s quality.

Conclusion

Of course, you might find you’re not yet to the point of testing whether a question will go anywhere. You might find yourself still in search of the question itself. And in that case too, the only thing to do is to keep asking questions.

A similar sentiment often attributed to Thomas Edison is pertinent here. When asked about his string of “failures” in trying to invent the electric light, Edison is reported to have said something like,

I have not failed. I’ve just found 10,000 ways that won’t work.¹²

Likewise, Seth Godin observes how one often has to do a lot of bad writing. As you do so, you get that bad writing out of the way, and better writing starts to flow.¹³

So it is with research questions too. Sometimes, you have to ask many bad questions in order to see how they lead nowhere and start asking better ones.

And if you’re ever at a loss for how to continue asking questions, queries like “How do I know x?” are often be a good place to begin. After all, in asking such questions, you’re explicitly pushing yourself to “see what is questionable,” to frame questions accordingly, and enjoy the task of exploring all the interesting trails those questions open up.

1. Header image provided by Oliver Roos. ↩︎
2. Hans-Georg Gadamer, “The Universality of the Hermeneutical Problem,” in Philosophical Hermeneutics, ed. and trans. David E. Ligne, 1st paperback ed. (affiliate disclosure; Berkeley: University of California Press, 1977), 12–13; italics added. Image provided by the Internet Encyclopedia of Philosophy. ↩︎
3. Hans-Georg Gadamer, Truth and Method, ed. and trans. Joel Weinsheimer and Donald G. Marshall, 2nd ed., Bloomsbury Revelations (affiliate disclosure; London: Bloomsbury Academic, 2013), 281. ↩︎
4. In distinguishing types of questions in this way, I’m indebted to the descriptions of “normal” and “extraordinary” science in Thomas S. Kuhn, The Structure of Scientific Revolutions, 50th anniversary ed. (affiliate disclosure; Chicago: University of Chicago Press, 2012). ↩︎
5. Kuhn, Scientific Revolutions, 91; see also J. David Stark, “Reading (in) Biblical Studies: Thomas Kuhn’s Significance for Contextualizing the Discipline,” Journal of Faith and the Academy 5.1 (2012): 40–54. ↩︎
6. Brevard S. Childs, Introduction to the Old Testament as Scripture, 1st American ed. (affiliate disclosure; Philadelphia: Fortress, 1979). ↩︎
7. Kuhn, Scientific Revolutions, 91. ↩︎
8. Gadamer, “Hermeneutical Problem,” 13. ↩︎
9. Gadamer, “Hermeneutical Problem,” 13. ↩︎
10. Gadamer, “Hermeneutical Problem,” 13. ↩︎
11. For these general angles of approaching problems with paradigms or what “everyone knows,” see Kuhn, Scientific Revolutions. ↩︎
12. The actual number of attempts cited in Edison’s sentiment seems to be the subject of some disagreement and variation. ↩︎
13. Seth Godin, Leap First: Creating Work That Matters, Audible ed. (affiliate disclosure; Louisville, CO: Sounds True, 2015). ↩︎