I’ve recently done some freelancing on Twitter about future research on political violence and thought I should make something a little more solid than tweets. In the political science literature on violence, my sense is that we’re starting to hit the flat of the curve on the conventional “why violence in village A but not village B?”-type question – unless you have a really innovative re-conceptualization or theoretical move, exceptional new data, or new methodological innovations. There’s still room to make big contributions there, but it’s increasingly tough compared to fifteen or even five years ago. It’s the same deal with a lot of important questions about the hard core of civil conflict (violence, organization, rebel governance, etc) – lots still to be done, but with an ever greater degree of difficulty.
For instance, the civil war onset literature has gotten pretty sleepy, with the exception of the enormously impressive and, I suspect, staggeringly expensive Ethnic Power Relations project – which is not even remotely the kind of thing an ABD can pull off in a dissertation. Nothing on insurgent organization (my own work very much included) is likely to have the same impact as Jeremy Weinstein’s massively influential Inside Rebellion any time soon, no matter how sophisticated or clever. Arjona, Kasfir, and Mampilly got into the rebel governance game in a way that will have people responding to them for a decade. The transition to normal science is important, valuable, and needs to continue, but changes the nature of the work.
Where I’ve been trying to move (starting in 2012, and most recently, and most focused on laying out a systematic empirical agenda, in 2017) is toward the “blurry edges” of civil war: topics that occur in the absence of a state monopoly of violence, but that don’t revolve entirely around a direct clash of arms between state and armed rebel. There’s plenty of space here to do new stuff, from conceptual work to nitty-gritty empirics.
The areas I personally find particularly intriguing include electoral violence (especially beyond election-season riots), criminal conflict, militia politics, armed political parties, state-armed group deal-making and cooperation, black markets, corruption within security apparatuses, drones, the infiltration of “mainstream” politics by non-state armed groups, how external states try to manipulate, prop up, or tear down actors within political systems, lynching and vigilantism, the behavior of internal security forces beyond COIN (killing dissidents, buying off opposition, shaping journalistic coverage, etc), and “dark side of civil society” actors willing to risk violence to in pursuit of hard-line demands (like the pro-blasphemy law protesters in Pakistan right now). I’m most interested in all of these things in democratic-ish places, since they can become intertwined with “normal” politics in fascinating ways.
Obviously, some of these already have substantial and important literatures already – but they seem ripe for further exploration as overlapping with the increasingly saturated civil war literature.The world is a lot bigger than the important but highly specific problems of insurgent mobilization and counterinsurgency. Eventually there will be a return to non-normal science on the narrower civil war side of things, so the field won’t continue to look this this forever. Electoral violence or militia stuff will saturate, and ambitious grad students will start saying “You know, we missed X in the COIN literature and here’s a way to totally rethink it ” or “here is a crazy new method that solves previously insoluble problem Y in the study of temporal-spatial patterns of micro-level violence.”
But for now at least, I think it’s a nice time to be pushing into cognate topics that look for cool new angles to research.
Paul Staniland 