Before I answer your specific questions about my book, let me first zoom out and comment on some broad, “meta” issues about how we, as social scientists, study social problems. That’s because all questions are embedded within a meta-intellectual environment that we rarely notice, let alone probe. Before we can appreciate answers to particular questions, we must first practice meta-cognition: reflecting on the questions we ask and the way we think. That’s usually how I think.

You shared with me an essay by Michael Desch, “How Political Science Became Irrelevant,” published in The Chronicle.1 I find it timely, thought-provoking, and wish that there were more of such reflections—however, while I agree with Desch’s lamentation that political science has become (or is becoming) irrelevant, I do not agree with certain aspects of his diagnosis. According to Desch:

The problem, in a nutshell, is that scholars increasingly privilege rigor over relevance … Relevance, in contrast, is gauged by whether scholarship contributes to the making of policy decisions … the social sciences have increasingly equated “science” with pure research, or knowledge for its own sake.

In my view, relevance isn’t only gauged by policy influence. And the crux of the problem isn’t that in pursuing rigor, we’ve sacrificed policy relevance but accumulated knowledge about epochal and disruptive patterns, i.e., “knowledge for its own sake.” Now, to be clear, there is plenty of excellent scholarship that has achieved both rigor and relevance and contributed tremendously to knowledge. My point is, if you analyze our disciplinary incentives and trends, that is, where we’re headed, the real problem is that we’ve specifically privileged “publication-friendly” rigor (a term I used in my interview with Stephen Dubner in Freakonomics, adapted from the industrial term “machine-friendly crops”)2—and, in the process, lost our relevance not only to policymakers but also to readers in general.
“Publication-friendly” rigor has two key qualities. First, the inquiry necessarily builds upon an established literature with stable, clear assumptions that does not require tedious on-the-ground investigation or “description” (the word that shall not be spoken). Second, the questions must be narrow enough to be precisely answered using standard linear causal assumptions (one dependent variable plus ideally two independent variables) and causal inference tools. The more established the assumption, the smaller the question, and the more precise one’s evidence, the less reviewers can poke holes in the analysis. Even novices quickly figure out that this is the path of least resistance.

At what price? The price isn’t, as Desch suggests, only policy irrelevance. The price is our ability to make sense of the world—particularly important, complex, disruptive problems—for ourselves, our peers, and any curious adult who wants to learn. This relevance is our fundamental duty as scholars.

Take Katzenstein and Seybert’s critique of “the ‘embarrassing’ and ‘dismal’ collective performance of the field of political economy in the years before the 2008 financial crisis.”3 The conventional literature’s assumption of stability and probabilistic risk, they argue, simply couldn’t account for disruptions. Or recall Hopf’s comments about the fall of the Soviet Union: “American social scientists did not look at the problem and then attack it with inappropriate theories and methods; they simply failed to look at the problem at all.”4

Publication-friendly rigor helps us know if micro interventions in a stable environment have an effect, and no doubt, that’s very useful. But insisting on this singular criterion of “rigor” and rewarding mainly, or only, this form of inquiry has been an impediment to knowledge about the issues that matter most: national growth, financial crises, great-power competition, etc.

That takes me to my book. Despite its deceiving title, How China Escaped the Poverty Trap, this book is meant to be a meta-critique of our intellectual paradigm—applied to reform-era China.5 As I argue, traditional assumptions of linear causality and tools serve us well when studying complicated worlds made up of discrete parts that do not interact with one another and evolve drastically over time (like toasters); they are supremely ill-fitted, however, for studying complex social realities comprising many moving parts and which produce unpredictable outcomes (like trees). The question of socio-economic transformation on China’s scale is definitely a complex, not complicated, problem.