The economist Tyler Cowen once formulated his three laws, of which the second is the most relevant to us today: “There is a literature on everything.” By this, he meant that there’s always prior research or writing on a given subject that will be useful to you—and which you should know and cite.
Cowen’s Second Law is, like this newsletter edition, a gentle rebuke to the absolutism of the novice researcher. Researchers at the beginning of their careers1 sometimes think that the most important quality of a research project is its novelty. Having heard from their advisers and their classmates that doing new work is exciting, they rely on a novelty heuristic. They assume that work that is newer must be better, and that, in turn, the most important work is the newest work.
Undoubtedly, as our plucky young researcher begins a project, they will read many scholarly books and articles that similarly claim to be the first to do X or the only study to do Y. In turn, they will often internalize the wrong lesson, believing that to imitate this success, they, too, should advertise themselves as being the first-ever researchers to do Z.
Everyone goes through this phase. Producing scholarly work requires distinguishing your project and framing its contributions. But good researchers learn to ignore the siren call of novelty.
In our view, the most important debates are the most enduring ones. The weakest justification for a study, after all, is to claim that it “fills a gap” in the existing literature. But novelty, by itself, is insufficient: what we value is the worth of a research project, and that has to be established by other means. In particular, if a question is worth asking, then it has probably been asked before, and that means that it is worthwhile to investigate those prior answers and see what they got right and wrong. After all, it may be that an afternoon spent with Google Scholar results will reveal that a beguiling question has already led a fleet of researchers to wreck their efforts on unseen difficulties. Or it could be that there are already lots of very good answers, in which case the value of addressing them will be very high but the effort involved in doing so will also likely be high, since you know the bar for making a contribution will be high.
But what if that afternoon in the library turns up few other studies? Certainly then we can declare that a project is new, brand new, totally novel, and important?
Well….no. For one, the words we use to describe projects change over the years and generations, and so it could be that there’s a huge literature just out of keyword reach. Consider how discourse about LGBT+ people has changed over the years and how hard it could be to find work from the 1970s using 2020s keywords. (One of us has written about marijuana policy, and for a good deal of the 20th century people mostly talked about “cannabis”, “pot”, or “marihuana”, requiring rather creative search strategies.) For another, it could be that there’s a large literature in a different discipline and so you need to use different parameters or bibliographies to find the right bread crumbs to lead back to earlier research. For yet another: English isn’t the only language in town.
Then there is the trouble of the “jingle-jangle” fallacy. Sometimes researchers think two different things are the same because they bear the same name (jingle fallacy); other times, they may find almost two identical or very similar things and claim they are different because they are labeled differently (jangle fallacy). The result? Both novelty claims that are simply not true and searches for literature that get cut short because the researcher doesn’t realize that there is other research outside of their silo that might be relevant to them.
We can promise you that, eventually, something relevant to your research interests will turn up… but it will take some creative sleuthing. It could be just a few grains of knowledge; it could be something wildly speculative; it could be something very old or very very new. It could even be something that you have to extrapolate from, like a general work (if you’re talking about war, for instance, it may be that nobody has written specifically about a given battle or regiment or weapons system—but somebody has written about the importance of battles, or tactics, or weapons in general, and you can hook back into their discussions.)
In our experience, Cowen’s Second Law is undefeated: you are always going to find prior research that’s relevant to your topic. And that’s good! You should welcome being part of a larger conversation. If you were really the first to add anything about a topic in general…well, you’d either be a genius for the ages or an incredible crank, but either way you’d probably be lonely.
The takeaway: Overclaiming novelty is a tic of the weak or insecure. It’s also likely to tick people off (because you’re ignoring their contributions) or to demonstrate that you’re unfamiliar with the literature (because you don’t know what does matter). Be confident in your contributions and clearly connect to what’s gone before. Just because something seems different doesn’t absolve you from trying to connect to the contributions that that research has made.
The practical: Given that there’s always a literature, you want to remember to be circumspect in how you describe your contribution. As always, it’s not the novelty but the value.
Don’t say there’s no studies about X; say, rather, that prior studies relevant to X have left Y or Z unaddressed.
Don’t claim to be first to study X in a Y way; rather, say that earlier works about X have been valuable, but by incorporating the insights of Y we can account for Z.
Don’t say that nobody has studied X in Y context; rather, say that by bringing X to the context of Y, we can realize Z potential gains.
You may also find useful:
“The Scholarly Literature”: Identifying “good” research begins by recognizing that single pieces of published, peer-reviewed scholarship are best understood as part of a lineage of scholarly work. Simply finding one or a handful of such papers or books will give students a rough snapshot of the sandbox in which they are playing, but only by reading widely and deeply will they understand the contours and nuances of the task at hand.
“The Limits of Originality”: Be clear in working with your adviser—and be clear in talking to yourself—about what you will be contributing that will be “original” and what existing tools (or data, interpretations, approaches—whatever!) will be based upon what others have done.
“Real Search Isn’t Google Search”: Convenient search engines are meant to optimize for convenience, not reliability or academic rigor. If you want reliable knowledge, you’ll need to use specialist tools.
Researchers in the middle of their careers and even researchers at the late stages of their careers are also occasionally guilty of this approach as well, in part because the incentive structures - fancy journal publications - generally demand splashy results…and what is more splashy than something new.