Stathis Kalyvas on 20 years of studying political violence

It’s been about 20 years, I think, since you first started publishing and working on violence. I believe some of your earliest work was on the Algerian Civil War ¹ and since then, you have been producing a tremendous amount of work. How would you characterize the evolution and development of the field? What are the trends that you’ve observed and how would you package that?

I would say that what my work did was to reconceptualize the idea of violence in a way that made it amenable to empirical research, especially violence within the context of civil wars. Up to then, we had a lot of work on violence that was theorized in highly abstract ways. When it was empirically oriented, this was done in a rather non-systematic way, obviously in a non-quantitative way, especially in history, and to some extent sociology and anthropology. So, in a sense, what I did was to take a concept that was hard to theoretically define and empirically measure and make it amenable for that. But it was also more than that because this reconceptualization pointed to all kinds of new and fascinating questions and, as such, it opened up a whole new research agenda.

Before I published the book, ² I realized that I couldn’t convince political scientists that violence was a topic worth studying in political science. All my early papers were rejected by journals, and people didn’t understand what I was trying to do. There was a lot of incomprehension that came from a long tradition in the field of international relations and the study of war, according to which war is defined as collective violence. Therefore, the fatalities of war were basically just an interesting manifestation of war itself as a phenomenon. People were studying war as a political and military process, but were not focused on its violence per se. They could not see the point. And to see the point, one had to approach this question from the perspective of civil wars, which at the time were not studied very much.

So, making the distinction between war and violence was very hard initially and only came to be accepted after my book was out, which, you know, made the case very thoroughly, in a way that was hard to do in the context of a journal article. My book also suggested a way of empirically studying that. After the book’s publication, there was, I would say, an explosion of studies, an explosion of work, following very much similar kinds of lines, micro-oriented, subnational, very much like your work as well, ³ trying to make sense of violence as a process amenable to empirical variation within a particular case. It also suggested a way to make sense through it of the larger political and social processes that produced this violence.

That was another problem, by the way—in the then nascent field of civil war studies, violence was used as a threshold to measure and characterize events as civil wars, which were then analyzed in an aggregate way, as opposed to their violence. That was again another difficulty, another obstacle in communicating and justifying my work. And, finally, there was suspicion for subnational research designs which were viewed as idiosyncratic, ungeneralizable case studies. So, what I did was to use the subnational framework to show that we could use quantitative methods within the context of a single conflict, that we could deploy the idea of variation along with the rich contextual research afforded by case studies, and that we could do all that to crack, as it were, the problem of violence.

There were a number of additional reasons why the field developed so quickly, and one of those didn’t really have much to do with academic research. It was basically politics. It was September 11 and its consequences. The US invasion of Afghanistan, and especially Iraq, in a sense brought back the old agenda of counterinsurgency studies, which existed then also in a very traditional way, and gave it both political pertinency, but also made it academically desirable, as it allowed access to tons of data and funding.

And so, the use of empirical techniques, the focus on variation, the focus on violence again became very popular, because they were seen as being policy-relevant. A field was born (with its various versions, such as “impact of economic interventions on counterinsurgency outcomes,” “development under fire,” etc.). And once you have a field, you have people who perpetuate it, which explains why this thing exploded.

The way I describe it here suggests a certain ambivalence about its development, because, first of all, I was never very happy about this direct policy relevance. When you study violence, you should be very careful, not just on ethical and moral but also on political grounds, about how people might grab and use your findings, because obviously they can be used in ways that inflict harm on people and also provide support for bad policies. And so that’s a very big problem.

My second concern was that even though a lot of the work was of high empirical (or should I say empiricist) quality, it very quickly acquired a certain opportunistic element: a lot of people were interested in getting data to use their tools on and publish papers without being really invested in understanding the actual processes in their depth, complexity, and implications. A lot of it became very self-referential, I think. So along with very important progress that was made and high-quality research, there was also this other aspect, this sort of opportunistic, policy, and professional-academic dimension, which created this situation in which I feel that even though we’ve improved our work on violence tremendously—we have a lot more data, we have more sophisticated tools, a lot of work is done now with geocoding, etcetera—it’s not clear to me exactly what the payoff has been in terms of real understanding, real learning. There is a lot of confusion as it is often the case with papers producing very contradictory findings that hinge of hundreds of minute differences in definitions, measurement, etc.

I was reading a review paper that Laia Balcells and Jessica Stanton ⁴ just finished about studies of violence for the Annual Review of Political Science and I came out of it feeling that I knew less about the question as opposed to more, because there is so much, you know, that is contradictory and very difficult to reconcile, because the parameters of those studies are not really explored in a systematic way and the question is sliced and diced in 10 different ways. So, a lot of studies, which are not exactly comparable to each other, are conducted and presented as contributions to the same question, and as a result we get lots of different findings that do not add up to something robust. Now, I am generalizing a bit here and I do not mean to imply that I disapprove of that kind of work. I think better data, better tools, more work, these are all necessary. There is a critique that says, “Now let’s throw the baby out with the bath water, everything that’s quantitative is a bad idea”—I obviously disagree with it. Indeed, Gilles Dorronsoro and his group have been arguing a very pointed critique along these lines: even though they describe it as an American or Anglo-Saxon approach to the study of conflict and violence—which clearly has an element of truth—it is phrased in a way that is just both too extreme and too superficial in my view. In the end, it does not really engage productively with the work that has been done and to just reject it wholesale and characterize it as sort of American imperialism, I think doesn’t make that much sense.

You realize that I’m very willing to be critical about the way the field has developed, but at the same time, I also want to take stock of its many positive improvements: the fact that we have a language, a vocabulary, that motivates a variety of researchers, and the fact that new data have been put together and analyzed in ways that can be replicable and productive.

Do you think the challenge is that the study of violence shouldn’t be a field? Or is it that we need more grounded research to try to understand what it is that we don’t know about the patterns researchers are inductively observing? Why do you think the field has taken this direction?

Clearly, the latter. I believe that the problems are related to the professional politics of academia. It’s easier in political science to publish papers that are well delineated: here is an empirical question, here are the data, here are the methods, here are the findings, let’s move on and repeat even if this does not seem to cumulate in the more or less definitive way of the hard sciences. And there isn’t enough of an incentive for people to do the more grounded, more time-consuming research that gives you more insights, which isn’t as quickly and as easily publishable. I mean, for me, my book took almost 10 years to produce and the whole system is stacked against that. When I started, I didn’t have tenure, so I took an enormous risk, which was in a sense rewarded, but for most people, this is a risk that is not acceptable, given their personal situation.

On top of it, what makes violence fascinating and exciting is that it’s by definition an interdisciplinary concept, a concept that is being studied by a variety of different fields from the hard sciences, like biology, then to psychology, economics, sociology, anthropology, history, literature, philosophy, you name it. It’s something that everyone is interested in and that is challenging as much as it is fascinating and productive because you get a variety of different insights. However, it’s very difficult to translate research from field to field given differences in emphasis, differences in vocabulary, differences in assumptions. But I think this is where the opportunity lies, in our ability to translate our findings for other fields, as well as to take advantage of theoretical and conceptual advances that are often produced there, and spark productive conversation between, say, historians and political scientists or anthropologists and political scientists, and so on. For example, while historians have a very deep understanding of cases that are relatively recent, for example, of decolonization, and political scientists are using data analysis to study the same process in an aggregate way, productive fertilization doesn’t happen as often as one would expect because, again, the structure of incentives doesn’t always help. People can be very defensive of their subfields and, frankly, quite parochial.

Do you have a rule of thumb for those interdisciplinary conversations? Is there something that scholars should aspire to when they are trying to reach across disciplinary boundaries?

Absolutely, but it’s something that cannot be done by committee, because when you have people coming with different agendas, from different fields, armed with different perspectives, very often trying to square their differences, you get bogged down in a Tower of Babel way, and you get something that very often lacks any strong sense of any particular content. What gets out of it is often very washed down in many ways. So what I think is needed is for specific researchers or teams of researchers to actually take the initiative to draw and translate from other fields into their own field and then produce that fertilization. But as I said before, it’s a risky undertaking for many researchers, because it’s time-consuming, the results are always unwelcome initially as they go against the existing grain, and a lot of people feel intimidated by this type of risk—and I do not blame them for that.

One of the things that you and I have talked about over the years is the distinction between micro and macro-orientations in studies of violence. Your work pioneered the micro, local dynamics and patterns of violence agenda. I’m wondering now how you see that, the bridging of the micro and macro and the ways in which it can most productively be handled.

In the last 10 years, I’ve become much more macro-oriented in my own research, but it’s a kind of macro that is fully inspired and driven by micro-level insights. And also, I am very cognizant of an additional layer, which I call the “meso,” the layer made of organizations, groups, etc. (as opposed to the country-level macro and the individual/event/locality micro). By relying on the insights that micro-oriented research produces, we can actually move up the ladder of abstraction in a way that’s much more meaningful and useful.

In this way, you can ask new questions, you can take the micro findings and problematize them at the macro-level, which I tried to do, for example, with my and Laia’s work on the meso-level changes brought by the Cold War and its end ⁵ and which is very much what I’m trying to do with my latest project, which is rethinking political violence as a more coherent field.

I guess one of the challenges that I’ve found—and my own work has gotten more macro over time—is I find it’s less satisfying in a way. I mean with the micro work, I feel like I can trace the instances of violence, as you did in the Greek Civil War, ⁶ at a house to house level, and it feels like I really have an understanding of the dynamics and the processes of mobilization and so forth, whereas with the macro, there’s so much abstraction that I find it harder to have the sense that I can get on top of it. How do you manage that, do you feel something similar?

I think you did it quite successfully with your latest work on genocide. ⁷ In a sense, you were inspired by your micro work ⁸ to see how that can generalize at the level of the African continent in your next book.

Thanks.

But you are right that sometimes abstraction can feel somehow cold and unreal. I would argue, though, that if abstraction rests on solid and real microfoundations (rather than some random assumptions), then it can be very useful and rewarding.

It’s always a matter of trade-offs: you give up some specificity in order to gain some generalizability. Intellectually speaking, one’s ability to move up and down the level of abstraction depending on the question one asks, or the confidence one feels, counteracts the very strong urge to specialize in an exceedingly narrow way. Very often, when you talk to people who do only macro work, you get the sense that they don’t really know what they’re really talking about: their categories are so abstract, so general, and their assumptions so unrealistic that, if you happen to have a sense of the underlying reality, you are really puzzled. In contrast, when you talk to people who do only micro, you get the sense that they know everything about what they study, especially anthropologists or micro-oriented historians, but then they can’t tell you something that’s a bit more general and more abstract. So, I find that when the same person moves up and down the ladder of abstraction, it’s a very nice inoculation against overspecialization, and at the same time, it infuses her work with many different insights that are otherwise hard to come by. Again, however, I would say that this presupposes the sort of privileged academic position that gives you the time, the confidence, and the perspective that allows you to really take risks and move out of your narrow comfort zone, while, in fact, very often, academia tends to be a sort of Fordist machine, in which you churn out articles and the only way to do that is by repeating the same thing over and over again.

Before we come to your next project, I want to ask you about the trade-offs and challenges of speaking to a general social science discipline versus doing research on a particular place? For instance, how was your work received in Greece? How did you negotiate both the specificity of the Greek Civil War and what you were saying about the Greek Civil War, with what you were saying to general studies of violence?

Well, my book hasn’t really been received in Greece because it was never translated.

Ah, okay!

In fact, I resisted its translation because I thought it wouldn’t be easy to understand for the generalist audience that would be attracted to it because of its interest in the Greek Civil War. It’s a highly specialized social science book, and people who are not versed in this kind of perspective, who don’t understand, for example, the idea of variation, would likely be confused by it, whereas specialists who all know English can access it directly from the original. However, I did publish a few papers written specifically about the Greek Civil War, following conversations with historians. My first paper was actually commissioned by a great historian of Modern Greece (among others), Mark Mazower from Columbia. We had a conversation, I told him about my findings, he was very surprised, so he asked me to write a paper about it, which ended up causing a tremendous uproar in Greece. ⁹ As a result, it forced me in quite an unexpected way to launch a completely different agenda in Greece, which is much more historical with a public history dimension, even though it’s of course infused by my social science work.

I have now another life as a scholar of the Greek Civil War in Greece and in Greek (and, more broadly, as a public intellectual), which is very time-consuming but also has been rewarding in different ways. I’ve used a different kind of language to speak to people about my findings to make them more interesting and relevant to them. They didn’t necessarily care about comparative and theoretical insights, they wanted to understand what the Greek Civil War was all about, rather than what all civil wars are all about. But of course, I wouldn’t be able to do the former without relying on my knowledge of the more general kinds of questions.

Do you have any general advice for scholars of violence who are balancing the specificity and the generality? Often, one faces very charged periods of a country’s political history and one also has to deal with the ethics of violence, of working with people who’ve suffered violence. I know in my own work it’s been a source of tension and consternation, of trying to be driven by social science principles but contributing to debates about a place where these debates are extremely intense, passionate, partisan, and controversial. And I just wonder if you had any thoughts on how to manage those tensions.

I basically made a decision early on to follow two principles. The first principle is not to advise policymakers, not to get involved in policy projects, because I didn’t want my work to be connected to issues of practice, for the reasons that I mentioned before and that you imply. And I followed also a second principle, which was not to engage with research as advocacy, to also keep it very academic vis-à-vis political advocates, who use these terms and these concepts to advance particular agendas, which may be right or wrong, but are political agendas, so to try to be as Weberian as possible in that respect.

It’s not an easy set of principles to follow because if you do refuse to engage with policy or advocacy, you cut yourself from a very active and fertile and interesting area, but one which I find very problematic ethically when it comes to my own research. For example, I was never willing to formulate my research agenda in terms of, say, counterinsurgency agendas, human rights agendas, or genocide agendas. Once you get into those fields, you lose both the necessary sense of distance that keeps you open to new discoveries and insights. In a way, I made a sort of exception to that in my work on the Greek Civil War because I got involved in public debates. But I tried to advocate not for any of the sides that fought in the Civil War but for a more “detached” perspective on the topic—although it is true that I ended up critiquing primarily leftist historians for the simple reason that they were the ones “owning the issue” and, therefore, setting the agenda.

Of course, you can draw all kinds of political and theoretical implications from this approach: distanced does not, and should not mean bland. However, I feel that if you fail to keep a healthy distance from this type of topic, you shouldn’t get involved because you will end up with eggs on your face and poorly done research.

Interesting. Okay, so could you tell me about the current book project, your motivations for it? And then we can talk a little bit about some of the grounding concepts and approaches.

Actually, this book project, whose tentative title is The Landscape of Political Violence, has very much been motivated by some of the things I just told you, namely, the idea that silos often hinder more than they help. ¹⁰ Over the years I’ve read very widely, and I found that there are all these established fields that very often ask similar questions. You raised yourself some of these issues in your own review paper on genocide. ¹¹ But these fields do not seem to be aware of each other’s existence, let alone speak to each other, and there seems to be an emphasis on policing boundaries between disciplines rather than on merging them. And there is also a general methodological issue: when we study, say, war or genocide, or revolution, we assume that there is a dependent variable so to speak, whose value is either the presence or the absence of that phenomenon. You have war or you have peace. You have genocide or you have absence of genocidal violence. But in fact, what I realize is that very often these categories are connected on some sort of a continuum. For example, the end of a war may lead to civil war, and the end of a genocide may open the way to state violence, and these categories may be causally connected, yet we tend not to formulate these types of hypotheses because if we did, we would be stepping out of our subfield. As a result, we are missing out a lot.

So I asked myself how we could rethink a more unified and coherent field of political violence that takes existing phenomena and their corresponding categories into consideration and redefines them in a way that minimizes their overlaps, summarizes most of their findings, and connects them so that we could formulate new hypotheses about the ways in which they interface and interact. It’s a pretty daunting task because there’s so much literature (and so much confusion). Perhaps for that reason, it is very exciting.

That sounds great. So, you define violence by the deliberate infliction of bodily harm. But there has been a distinction, and partly inspired by your work, about violence as bodily harm against people not engaged in armed conflict, and war as combatant on combatant violence. And it seemed to me, in this forthcoming book, you would be breaking down some of those distinctions. If so, could you tell me the thinking behind that?

You can still maintain those distinctions within the bigger categories I propose. For example, in the study of war, you can have violence between combatants and violence against non-combatants and the same is true about civil war, etc. You can focus on one (as I did in my work on civil wars), the other, or both. However, you are right to say that I view violence as the infliction of bodily harm to push back against the tendency to broaden the concept of violence so much as to include things like poverty or injustice, which then make the study of violence as infliction of bodily harm all but impossible because you get into endless debates about everything that’s bad, or everything you think is bad. In this perspective, racism as a set of attitudes becomes an instance of violence which can’t then be distinguished from racist motivated violence. Low worker compensation becomes an instance of violence. Environmental depredation becomes an instance of violence. Eating meat becomes an instance of violence. But then, it becomes completely impossible to study violence as bodily harm. Of course, this is a choice that can be described as ideological. By narrowing the scope of the concept, you’re making a set of assumptions that have ideological extensions. But I go back to my position as a Weberian social scientist and say, “Well I’m willing to bracket those other things out.” I don’t want to say that these things are bad or not bad or anything. But I want to be able to study the narrower version of violence because what I care about is understanding it for what it is. And the subset of violence as bodily harm is so enormous that it’s really daunting to begin with—if you open it up even more, you end up basically conversing endlessly and perhaps repeating clichés, rather than really making important advances.

Which allows me to go back to the policy dimension that I mentioned before: as I said, I don’t want to give advice to users of violence, but I want to be consistent. So I don’t want to be advising people whose objective is to end any violence on the planet as well. It’s impossible to be everything to everyone. We live in a time where these kinds of choices are now being challenged from outside social science, where everything is seen as being ideologically oriented and therefore suspect, and from within social science, where you have to be policy-oriented since it’s the state that primarily funds research. So, I am not advising the prince nor do I advise the anti-prince crowd either. I see myself as a scholar who tries to make sense of the world and offers the fruits of their research to the world.

But don’t you think that by choosing not to study structural violence—poverty, these other forms of invisible violence and inequality—that’s another ideological choice?

No, because I don’t reject the study of poverty at all. What I am saying is, study it as poverty. Now if you want to characterize poverty as violence, that’s also OK as a general normative assumption but don’t mix the empirical and theoretical study of poverty with the study of, say, violence in civil war because these are not the same.

You chose 11 types of violence. Tell me about that choice. What are they and why those 11?

I made two initial choices in this project. First, I wanted to focus on aggregate macro-phenomena, rather than repertoires [of violence], which are endless. Torture is a repertoire, whereas war is a macro-phenomenon that includes a variety of different repertoires, such as torture, rape, aerial bombardment, etc. And, second, I wanted to use categories of violence that already have an existing literature attached to them, which means they’ve been in a sense selected by the community of scholars over the years as making sense to them. Even when they’re problematic, especially genocide and terrorism, they have been the object of sustained study and research. So, my intervention is basically to try to redraw their boundaries, not to try to get rid of them, to see how I can still keep them in the analysis, because I believe that their core is associated with a particular form of violence that has some unique characteristics.

I’ll give you an example about terrorism. If you look at the datasets on terrorism, which is defined mainly as rebel violence, a huge proportion of it is the violence of rebel groups in civil wars, which does not really correspond to our instinctual understanding of terrorism as an activity that is not mainly rebel violence in civil war. Now, you can still have terrorism within civil war but this is distinct from categorizing all rebel violence in civil war as terrorism. I was going over a paper recently where someone was focusing on how migration impacts terrorism. And what was basically meant by that was violence against migrants. And the finding was presented as “migration causes an increase in terrorism” because there, natives attack migrants. But this is incredibly confusing because I thought that the paper was going to tell us whether migration causes either natives to launch terrorist attacks against migrants, not any attacks, or that migrants launch terrorist attacks against the authorities of their host state. To define terrorism so broadly I think does a disservice to our understanding.

So, do you have a working understanding of terrorism?

A lot of what I’m doing is basically relying on existing work. So, there is a very small minority of scholars of terrorism who understand it as a form of clandestine violence by non-state actors who do not control territory. ¹² And I think that this understanding gives us a good handle to isolate what I take to be the essence of the concept of terrorism from all the rest, which is better thought out as part of different categories, such as civil war, etc. Now, the majority of students of terrorism won’t like that. They’re not likely to accept it because essentially it will shrink their field empirically—though I believe it will strengthen it in the long run.

What’s the importance of not holding territory?

It drives you to a logic of action that’s fundamentally distinct: clandestine political actors, actors who do not hold territory, have to relate to civilians in a different way, operate in a different way, have different kinds of resources, have to aim for different kinds of goals, and so on and so forth. Now, you can have terrorism, defined as clandestine violence, within civil war, when an insurgent actor operates outside of the territory they hold. For example, Sendero Luminoso in Peru operated as a typical insurgent actor in the countryside, but then exploded bombs and followed similar tactics in Lima in the capital, where they didn’t really have a territorial presence. In other words, Sendero in Lima operated in ways that makes it of the same type with actors such as ETA in the Basque Country. One of the benefits of this approach is that it allows for connections between the different categories of political violence. In fact, I specify four different sorts of connecting logics.

And what are those four?

The first one is a logic of hierarchy whereby a category of political violence generates the conditions for the emergence of other categories within it; the latter arguably would have not appeared otherwise. For example, some interstate wars have been credited with enabling genocide and ethnic cleansing; also they sometimes might spark civil wars, as in Iraq following the US invasion. Or civil war might enable the rise of organized crime, as was the case in the former Yugoslavia. In other words, the basic intuition here is that one category of political violence emerges and operates within another one simultaneously, but without this process being intentional.

The second connecting logic is transformational, whereby one category of political violence transforms into, and is superseded by, another one. For instance, large-scale mass protests might mutate into a civil war, as was the case in Syria in 2011; a political assassination might escalate into civil war, as was the case with the assassination of Jorge Eliécer Gaitán, the leader of the Liberal Party of Colombia, in 1948 which led to a full-fledged civil war known as “La Violencia”; or the failure of a military coup, such as the one led by Francisco Franco in Spain in 1936 might open the way for a civil war. Or take, for example, the research on post-conflict violence by e.g. Séverine Autesserre. ¹³ The war in the Congo ends, yet “post-conflict” violence emerges. We have a hard time dealing with it because we have been conditioned into thinking that the absence of war is peace.

The third connecting logic is instrumental: a category is deployed because it explicitly helps implement another one. For example, intercommunal violence is sometimes used to help achieve genocide, as was the case in Rwanda. Unlike the transformational logic, which is typically unintended, this one is explicitly deployed in order to produce another category.

Lastly, the fourth connecting logic is one of substitution, whereby one category of violence emerges because another one is unavailable or impossible. The Cold War can be thought of as a period when internationalized civil wars (or “proxy wars”) became a substitute for an impossibly destructive frontal clash between the United States and the Soviet Union. A substitution logic has been documented between terrorism and civil war: terrorism can be understood as a substitute for (territorial) civil war, by rebels operating in the context of very strong states who prevent them from launching a full-scale insurgency; terrorism, in that framework constitutes a non-territorial insurgency. ¹⁴ Likewise Philip Roessler has pointed to a substitution logic between military coups and civil wars in ethnically divided societies of sub-Saharan Africa: African rulers face a trade-off when it comes to power-sharing. On the one hand, they face a high likelihood of being overthrown in a military coup by members of their own military-political faction who also have ties with a different ethnic group. On the other hand, however, if they exclude them from the ruling coalition, they face the danger that these individuals may mobilize their ethnic power base to launch an insurgency against them. Given this stark choice and the fact that rulers are more vulnerable to a military coup than a civil war, they are attracted by the choice of exclusion, leading them to increase the likelihood of a civil war. In this formulation, civil war represents the consequences of a strategic choice by rulers, backed by their coethnics, to coup-proof their regimes from their ethnic rivals. ¹⁵

What differentiates the second set of logics (instrumental and substitution) from the first set (hierarchy and transformation) is a much more direct sense of agency.

Tell me about the process: How do you go about doing this type of synthetic work?

The obvious way is to read a lot of what people have written and to try to abstract from it by identifying its essence, so to speak, using a novel theoretical perspective. Like all synthetic work, it’s a sort of back and forth between messy complexity and reductive abstraction.

How do you make the distinction between what to leave in and what to leave out in your 11-category typology? Where do riots, massacres, or rape in civil war for instance fit in?

I have settled on 11 types through a process of elimination and by examining past efforts. They are the following ones—though I am still trying to work out some issues with labeling: (1) Interstate war, (2) Civil war, (3) Revolution/insurrection, (4) State violence, (5) Genocide, (6) Ethnic cleansing, (7) Military coup, (8) Political assassination, (9) Terrorism, (10) Intercommunal violence, and (11) Organized crime. These are all macro-level aggregate phenomena that have been studied extensively and have given rise to large bodies of research. They can be observed as independent, self-contained phenomena, although they are linked to each other following the connecting logics I just discussed. These macro-phenomena are different from repertoires of violence, such as massacre, rape, or torture that can occur within all these categories. They also must satisfy the twin conditions of mutual exclusivity and joint exhaustiveness. Mutual exclusivity calls for the elimination of overlaps between categories. For example, a civil war cannot be “coded” as an interstate war and vice versa. And joint exhaustiveness implies that the set of proposed categories captures the entire spectrum of political violence as per its definition. That is, all instances of political violence can be coded into any of these categories.

An added benefit of this approach, I believe, is that it offers a vocabulary to describe complex events that often combine different categories of violence. For example, the Irish Troubles are notoriously hard to describe: Are they an instance of terrorism, civil war, “sectarian” (i.e. intercommunal) violence or state violence, among others? Using this approach, we can say, “Well this started as an insurrection, then it became a civil war in certain parts of the country, terrorism in others, and in some key points it led to intercommunal violence.” Instead of fighting for a single overarching description we can disaggregate this historical event into these categories and study how they are related to each other, which I think gives us the ability to shed new light on them. What do you say, have I convinced you?

It strikes me as incredibly ambitious, Stathis, and if anyone can pull it off, you’ll be able to pull it off! But it’s tricky. It seems every choice you make, you’re going to be leaving certain things out. I think there are many minefields in this project, so to speak. When I first started teaching a graduate seminar on political violence, I came at it from a similar perspective. The scholars working in different areas of political violence were not speaking to each other—and I thought that we should strive perhaps for a more unified theory of violence, but I gave up over time because I felt that it was such a disparate agenda. But I don’t know if that was the right decision, I just got frustrated over time.

It’s very frustrating indeed, but one of the choices I made is not to try to come up with a general theory of political violence or to argue that this is the only way to conceptualize political violence. Coming up with a set of hypotheses or some general conjectures is as far as one can get to at this stage, I think. If on top of it, you go for a single, general theory, then it becomes so extensively ambitious that I think it can defeat you very easily, so that was a choice I made as a way to go ahead with this. And, obviously, I want to make the case that this is both a reasonable and useful way to rethink political violence rather than the only possible way to do so.

I like your efforts to bring some order on the field in the sense of your two-by-two table where you’ve got state and non-state perpetrators and state and non-state victims, and then being able to locate different types of violence within that two-by-two. I found that to be really compelling and fruitful analytically. Your arguments about the linkages or the substitutions or the ways in which the absence of one type of violence might produce or create incentives or possibilities for another type of violence is a really productive insight as well. Where I was getting stuck was the overlap between some of the categories, or what was in and what was out. Intercommunal violence, for example, struck me very much because it could be a part of ethnic cleansing or genocide. But how you can have intercommunal violence within a state-directed phenomenon? That didn’t satisfy for me the aggregate or exclusivity parameter. And then interstate war—which was in your category of state perpetrator—felt like a really different kind of violence.

Well, choices are hard and, as I said, I’m still working on these categories. To use your example, intercommunal violence is an independent phenomenon that has been studied quite extensively by, among others, Donald Horowitz, Ashutosh Varshney, Steven Wilkinson, or more recently Jana Krause. ¹⁶ There is now a dataset dedicated to it and it is quite widely used. So, the category is there, and it is being used. At the same time, it is true that it is connected to other categories of political violence, such as ethnic cleansing or genocide, and the instrumental logic I described captures part of how. However, ethnic cleansing and genocide are distinct, independent phenomena that are not exclusively associated with intercommunal violence, that is, they exist independently of it and have distinct characteristics, such as state planning, etc. A lot of the difficult debate going on around the fate of the Ottoman Armenians is related to our inability to clearly differentiate between genocide, ethnic cleansing, and intercommunal violence. We won’t resolve it, obviously, with my method since the disagreement is about placing blame, hence eminently political: to call it ethnic cleaning or intercommunal violence gone wrong rather than genocide has clear political implications—and hence motivations. However, we can clarify the scholarly debate by using a clear terminology—and indeed, the serious scholars who study this topic refer in many ways to these categories implicitly rather than explicitly or in a disciplined way.

What about rape in civil war or rape in general?

Again, rape is a repertoire that can appear in any category of political violence, or non-political violence for that matter. But then, we can ask an empirical question: Are certain repertoires only or primarily associated with certain categories? Why do certain repertoires recur in certain categories—or in certain categories during certain times or in certain places? Again, that’s a question which is harder to ask outside of a general framework, although people have been asking about variation in repertoires of violence across civil wars, actors in civil wars, or places within civil wars. Yet, because the language, the vocabulary, is not always helpful, they don’t ask it in an optimal way, whereas I think these are fascinating questions.

Totally. How do you imagine structuring your project? Will each type be a chapter?

Yes. There is a theoretical introduction, which includes an intellectual history of the field, because it turns out there was a substantial literature during the 1960s that uses political violence as a unified category, with people like Ted Robert Gurr and Douglas Hibbs. ¹⁷ They use these incredibly complicated factor analyses of the time where everything is related to everything else! In a sense, I am trying to resurrect that agenda which I was surprised to rediscover, but without the hubris of coming up with a general theory and taking into account all the work that has been done since then, which, although fragmented, is pretty impressive.

And then there’s a chapter for each type, where I engage with existing definitions and understandings. There is, for example, a very interesting new book manuscript by Mark Beissinger, which I think is extremely insightful. But even though he makes a very interesting point about how revolution has been transformed, he merges the concept of revolution as a street action with that of revolution as insurgency. So you can have the Arab Spring and the Chinese Revolution/civil war together. And, of course, one tends to be urban, and the other tends to be rural. And so instead of making an argument, which I think makes more sense, about how certain civil wars are giving way to urban revolutions, he argues that revolutions are being transformed, which is not necessarily a different thing but it is potentially less compelling and more confusing given that there is an entire field that studies the Chinese Revolution primarily as a civil war (but, again, the logic of connections is helpful in that we can see this historical phenomenon as an aggregate of different forms of political violence). Nevertheless, this is very much going in the direction that I advocate. So, in every field there is good interesting work that tries to push the boundaries of what we have been doing. What I bring to it is a theoretical umbrella, so to speak, along with a bit of, hopefully, more conceptual rigor.

And then the third part of the book would be about the four logics of connections that I described above, the hypotheses that can be derived from them, along with illustrations, redescriptions, and theoretical conjectures. That’s the basic idea. I would like it to be an agenda-setting book, not in the sense that people are going to necessarily buy the argument—I think there’s going to be pushback which is OK—but in the sense that people are going to be engaged by it and inspired to ask new questions—or, rather, old, enduring questions in new ways.

That’s great. What about the distinction between selective and indiscriminate violence, which was such an important part of The Logic of Violence in Civil War? How do you see that fitting into the typology?

Again, it can appear in all different categories—and then you can ask again the question: Is selective violence more likely to emerge in certain categories, as opposed to others? But, in general, and without having conducted that study, I can tell you that state violence can be selective or indiscriminate. Likewise, intercommunal violence can be selective, and it can be indiscriminate. For example, the somehow hard to classify “hate crime” can be thought of as a disaggregated version of intercommunal violence which is an interesting way to think about it, because presently it is used generically and can be applied to everything in a sort of unthinking way: why not get rid of genocide and use hate crime instead, etc. It becomes so common that all violence in any form of violence is a hate crime.

Okay well, I can’t wait to see it. That sounds awesome. Let me ask you one more question: Would you have any advice for graduate students who want to do work on violence?

I have a difficult time advising them because on the one hand, I want to tell them to spend a lot of time on their thesis, to be committed to what they do in the sense of not being opportunistic, yet, on the other hand, the structure of incentives, driven by lots and early publications, makes it very hard to take big risks and go deep. And frankly speaking, I don’t know how to square that. I am reluctant to advise students to take this kind of big risks, to do things that are harder, but at the same time I dislike the fact that everything is driven by narrow professional considerations rather than intellectual ones. Perhaps, I should try to attract students who are willing to go down that road despite everything. But I don’t have an institutional solution. If you have one, I’m ready to listen to it.

I really struggle with this issue too, that’s partly why I ask it. My inclinations are to do more in-depth work in a particular place and to understand it very well—and to have it be systematic and rigorous and theoretical. But that tends to produce book-length work rather than article-length work. And such work is just not as legible on the academic market [in the United States] whereas the most sophisticated new method tends to receive the most attention.

The publication imperative creates a lot of artificial, I would say frankly useless knowledge.

Yeah.

I feel that we don’t prize the “truth” if it is not required to achieve publication. We tend to prize, I fear, whatever makes the paper more likely to be published. And this is not necessarily the truth, at least not always. I think there is perhaps a case to be made for work that is theoretically less innovative, but descriptively rigorous and more honest, so that it can be really used by others. I think good description is something that is certainly more useful than bad theory and often as useful as causal inference.

It’s true. From my perspective, if we think about what as a discipline we’re contributing to is, provide a rigorous, well-researched account of what happened. And that often has durability for decades. However, that good analytic description tends to be de-emphasized now, contrary to theory and causal identification. I come from a particular position but when I put on the hat of someone from a different discipline and think, “Ok well, what can I learn from this work?” it’s often so wrapped up in a set of assumptions about what political science is and who it’s speaking to that it just becomes narrower and narrower. I think we are more and more speaking to one another rather than speaking to the broader phenomenon that we’re trying to study and people who are interested in that broader phenomenon.

But there is a more radical critique, which is not that we’re just being narrow: we’re also very often systematically wrong, because we privilege tools over substance and sometimes those tools push us toward systematically misleading directions.

I don’t know if I’d developed that particular conclusion myself, but if that’s the case then that is worse, yes. Then incentives are completely perverting our inquiry, which is deeply problematic. How do you see this playing out for political science?

I do believe that, especially in large academic markets, there is room for segmentation, and I think that if you throw out things that are of high quality even if somehow heterodox, they will find their niche, and so that’s what I have decided to push my students to do, i.e. to do things in that direction. If they then find a job in academia, fine. But if they don’t, they will be able to find policy jobs, government jobs, think tank jobs, and you know, their work is going to be out there, and perhaps somebody in academia will still read it, and it’s going to fertilize somebody else’s agenda, and you never know how these things might work in the long run. In short, I am still optimistic.