STATHIS N. KALYVAS
▶ FIELDWORK LOCATION: GREECE
The story of how I got to conduct the fieldwork that ended up in my 2006 book, The Logic of Violence in Civil War, illustrates the significance of chance, randomness, and serendipity in conducting research.
It all goes way back to 1988, when I was accepted to the graduate program in political science at the University of Chicago. At the time, Chicago had a policy of accepting (many) more students than it could fund, and then effectively conducting a grueling and stressful funding selection process in-house. As I was admitted with no funding, my only option was to accept a Fulbright scholarship that I had been awarded in Greece. This scholarship was good for just one year and also came with the so-called two-year home requirement, a provision intended to stem the brain drain to the United States. It basically obligated you to return to your country after obtaining your PhD. Say what you want about Chicago’s policy (which the university phased out a few years later), but without it I would not have been admitted in the first place. I am grateful to have been given the opportunity to take Chicago’s offer and eventually receive funding from the university.
Fast forward a few years. After completing my studies, getting my PhD, getting a first job at Ohio State, and a year later moving on to NYU, I had to face the music. The two-year home requirement had been in the back of my mind, but with a tenure track job at a good university, I thought I would find a way to bail myself out. How wrong I was. When the moment came for me to switch status and apply for permanent residency (the “green card”), I was told by NYU’s International Office that it would be pretty much impossible unless I managed to obtain a waiver from the relevant agency (in this case, the United States Information Agency [USIA]). I did scramble to apply for a waiver pursuing a number of different legal paths, but eventually I learned that all of my applications had been rejected by the USIA.
I had no option but to leave the country.1 So one night in the fall of 1997, I packed my suitcases as the chairman of the department wished me “a nice exile,” and I flew back to Greece on a two-year leave of absence with a year off my tenure clock and no salary. I had to scrap my main project at the time (a study of polarized politics) because I couldn’t conduct its demanding library research in Greece and the internet was still in its infancy. I could finish a couple of papers, but with time on my hands, I began to seek new research possibilities.
A conversation I had with former Chicago PhD classmate Roger Petersen in New York just before my departure sparked my interest in studying conflict. Roger was a pioneer in the study of civil conflict. I still vividly remember reading his dissertation proposal on an announcement board at Chicago. His creative combination of rational choice theory (imparted by Jon Elster), network analysis (inspired by John Padgett), and security studies (John Mearsheimer’s contribution) to explain the choices of Lithuanian peasants during and immediately after the Second World War caught my imagination: this was methodological eclecticism at its best applied to a fascinating topic. At the time, however, I was working on a completely different (and equally fascinating) topic, the emergence of Christian Democratic parties. Roger then moved to Saint Louis to take a job at Washington University, and we got quite out of touch—remember, this was before the internet! I only saw him again a couple of years later, when he came to NYU while on sabbatical. I shared with him my predicament and asked him about his research, which resulted in a conversation that rekindled my excitement. I had been curious about the Greek Civil War, partly because I knew very little about it, and this conversation got me thinking about using my time in Greece to conduct a small project to learn about it. Reading Roger’s work,2 I was particularly attracted by his “on-the ground” perspective, and I thought it would be a good idea to do something along those lines. However, unlike classic ethnographies I had read and admired a great deal,3 Roger managed to combine interviews with a strong theoretical agenda and a compelling research design—an unusual combination reminiscent of another book that had caught my imagination, my advisor David Laitin’s Hegemony and Culture. It was around that time that I read Diego Gambetta’s, The Sicilian Mafia, a book that helped me absorb this type of research.4 This book resonated with an earlier experience I had had as an undergraduate student, working as an enumerator for a large psychological and medical survey conducted in the Greek countryside. I had discovered that I loved hearing people talk and, most important for the case at hand, that people exhibited a propensity for relating their experience. In short, many streams converged in quite a subconscious way during that time.
After returning to Athens and embarking on this odd two-year exile, the first thing I did was consult some established Greek historians of the period about my idea. They were quick to disabuse me: “Don’t even think about interviewing survivors,” they said, “most won’t talk, and those who would will lie.” Of course, they had interacted only with important figures, political and military leaders or leading intellectuals, rather than with ordinary people. With few exceptions, historians had very little interest in the experiences of country folk and were extremely suspicious, if not outright dismissive, of oral testimonies and local research. Anthropologists were much more open to these approaches, but they were equally suspicious of any inclination toward theorizing systematic empirical patterns and quite disdainful of approaches that took rationality seriously.5 As for political scientists, steeped in the study of elections and parties, they were openly puzzled about why anyone would want to embark on such a wild topic.
But where to start? Again, Roger’s experience inspired me; he had stumbled on his own research by chatting with immigrant Lithuanian families in Chicago while working as a salesman of Eastern European household goods. The initial challenge was to locate “ordinary people” who could share their experiences of the civil war. I began by asking my friends to tell me about their grandparents, and I quickly realized that most of them had indeed had all kinds of traumatic experiences that I had never suspected. I began meeting with them without really knowing what to ask and discovered that they loved to talk and had a lot of stories to tell, although they were utterly confused about details, dates, and the sequence of events. It all sounded fascinating and bewildering at the same time, full of intriguing details that were hard or even impossible to make sense of, or verify.
That experience convinced me that the only way to make sense of these stories was to focus on a particular geographic area, to minimize the “noise” and try to triangulate this baffling mass of information. Using my network of friends’ grandparents and proceeding by snowball sampling, I did a few pilot trips in several areas of Greece. In one of them, I stumbled into a former classmate of mine at the University of Athens who had become a judge in the provincial town I was visiting. I went ahead and asked him whether he knew if the courts kept archives from the civil war period—there were few open state archives covering that period then. He took me to the basement of the court building, where lo and behold tens of unopened, huge bags full of papers were rotting away. Once I had opened some of them, I realized that the material they contained was precious. Although judicial documents incorporate all kinds of biases, they also contain extremely valuable and detailed information. At this point I had my first research epiphany: I would focus my fieldwork on this particular region; perhaps this could even turn into a bigger project than I had initially planned!
The research question I had set out with was pretty straightforward: How do individuals pick sides in civil wars? Once I started interviewing people and mining the archives, I came to the realization that many people’s “choices” were in fact endogenous to a variety of complex factors and would be extremely difficult to disentangle. I also realized the important role violence played in that process, something that had not occurred to me because my understanding of civil wars at that point focused on their political rather than their military aspects. Hence, having realized the importance of violence as an important independent variable of political behavior, I gradually opened up to thinking of it as my dependent variable.
Armed with increasing local knowledge generated from the intensive archival research I was conducting, I began structuring my interviews around the details of the events that had taken place in that region rather than the set of vague, preconceived notions I had been carrying around in my head. For example, influenced by Barrington Moore and Theda Skocpol, I had thought that civil wars were fundamentally instances of mass mobilization—uprisings—with people coming together around a set of grievances to challenge the existing regime.6 Indeed, this is what social movement theory and the theory of social revolutions—and also the historiography of the Greek Civil War—had taught me. Yet what I was finding pointed to a much more complex, sequenced process whereby violence often came before mobilization and triggered it endogenously, as well as ultimately molding the political identities that would come to define the conflict. It took me some time to come to the realization that the “data” I was collecting was forcing me to question my own assumptions. Once I became fascinated by the transformative power of violence—a fact that I had not anticipated—I completely reframed my research question. Instead of asking how people made their choices, I decided to focus on the logic of violence and how it constrained and even generated people’s choices. It was extremely difficult for me to publish papers at this stage because this idea was not widely understood or accepted; it required a theoretical and conceptual apparatus that was just not obvious. I needed to build a theory of insurgency and nest within it a theory of violence. In other words, I had to write a book. That was going to take a long time, a lot of effort, and require considerable confidence in my ability to carry it to fruition—at a time when my tenure review was coming up. In the end this gamble paid off, but there is no denying the professional risk it entailed. However, I was so taken by the project that I did not hesitate. And here I have to thank my other doctoral advisor, Adam Przeworski, for encouraging me to undertake such a risky project. No matter how strongly one feels about a project, encouragement from a mentor or trusted senior colleague can be essential.
How about hypotheses? I was taught that the way to do research began with theory and was followed by the formulation of hypotheses, the gathering of data, and the testing of these hypotheses, leading to the confirmation or falsification of the theory. But I was doing everything in reverse: I started with fieldwork to collect data without a clear idea of what exactly I was seeking. In turn, the fieldwork forced me to ditch not only my initial insights but also my original research question. I had to formulate a new question, generate a new theory, which I then had to test with new data and more fieldwork. Fortunately, I could stagger my fieldwork in small increments. Six months into my exile, I applied for postdocs and was lucky to get one at the European University Institute in Florence. This gave me the time and ability to work on the theory, which I was able to “pilot,” as it were, by writing a study of the dynamics of violence in the then ongoing civil war in Algeria that had begun in 1992.7 The postdoc also gave me time to put together a much more coherent grant proposal than I would have been able to write before this process began, which ultimately funded the bulk of my fieldwork.8 In addition, traveling back and forth to the field was much easier flying to Greece from Italy rather than from New York.
Needless to say, I redesigned my fieldwork and tweaked my research design to reflect all of these developments. Instead of studying a region in a purely ethnographic way, as I had originally planned, I decided to combine ethnography and quantitative data collection. I would research the local history of every village in the region with the aim of generating a data set that would enable me to test my hypotheses locally yet systematically. At the time, most comparativists tended to dismiss local studies as “case studies,” at best, or parochial, at worst—indeed, I still occasionally run into descriptions of The Logic of Violence in Civil War as a study of the Greek Civil War. By using homicides and villages as my unit of analysis, I was able to combine the local and the large-N into what is now known as a “subnational” research design, thus spearheading what would become known as the “micro-turn” in conflict studies, at a time when cross-national, macro-level studies dominated the field.9 Needless to say, this was incredibly labor-intensive. I had to visit more than sixty villages and identify informants in each of them. After I was done, I replicated my study in another region of the country and built another data set covering the entire territory of Greece using a variety of published (mostly local) sources to run additional tests. At the same time, I collected a considerable number of qualitative observations from a broad cross-section of conflicts worldwide. Following publication of my book, I discovered the existence of a unique data set, the Hamlet Evaluation System, which had been designed and used during the Vietnam War and had a logic compatible with that of my study. I was thus able to conduct additional out-of-sample empirical tests.10
It is important to add here that this empirical strategy was anchored in a robust theoretical structure. Initial fieldwork produced several intuitions that were subsequently filtered through broad comparative reading; in turn, the intuitions that survived this filtering provided the foundations for a theoretical model that led to fully formed empirical characterizations and hypotheses.
The takeaway of this story ought to be obvious by now. Field research (and research more broadly) is a highly dialectical processes that requires constant movement between theory and data. I find the current trend of overengineering and isolating research design, theory, and empirical research by means of watertight procedures (such as preregistration, preanalysis plans, etc.) to be potentially limiting, perhaps even counterproductive—as is the imposition of complicated and ever-expanding standards for the collection and handling of qualitative evidence. What makes fieldwork potentially so rewarding and meaningful is its simultaneously structured yet fluid quality, the fact that it can open us up to a hitherto unsuspected reality. In short, rather than trying to fit fieldwork (and empirical research more broadly) into what is effectively a Procrustean bed, we should allow our research to guide us.
I am aware that this recommendation might sound heretical, tantamount of caving in to our own implicit biases. The absence of a watertight separation between theory and research design, on one hand, and data collection, on the other, is increasingly considered inappropriate at best, potentially dishonest at worst. I understand the logic of such a view and accept that it might make sense when dealing with certain types of mostly narrowly framed data collection and estimation procedures—most notably surveys and experiments. Nonetheless, I believe it is important to allow enough room for fieldwork, and empirical research more broadly, to guide the process of theorization—and, in turn, for theorization to allow us to distill empirical complexity into empirical “essence.” More often than we like to believe, our empirical and theoretical priors tend to be crude and potentially misleading approximations of the phenomena we study. As a result, sophisticated empirical research is often designed on the basis of underlying theoretical assumptions and empirical scope conditions whose validity is far from given.
Instead of trying to force these phenomena into these priors, we have much to gain by allowing the field to guide us: at the very least by allowing us to correct faulty assumptions, but sometimes by pushing us to reorient our research and open new theoretical vistas. Elizabeth Kolbert recounts the story of how, during the 1980s, scientists were able to successfully revise the causes of the destruction of many organisms sixty-five million years ago, most famously the dinosaurs, an event known as the “Cretaceous-Tertiary extinction.” This revision was triggered by the work of a geologist, Walter Alvarez, who had originally embarked on a study of how plate tectonics led to the emergence of the Italian peninsula. In the process of his research, he came across a thin layer of clay containing an unusually diverse and large number of uncommon fossils. This discovery suggested to him that they had disappeared abruptly, eventually leading him to question the then dominant theory that posited the gradual disappearance of organisms, known as “uniformitarianism.” In turn, this led to the formulation of an alternative theory, that of the catastrophic consequences of an asteroid impact. As Alvarez told Kolbert, “Here you have a challenge to a uniformitarian viewpoint that basically every geologist and paleontologist had been trained in, as had their professors and their professors’ professors, all the way back to [Charles] Lyell.”11 In short, this unexpected fieldwork finding totally unrelated to Alvarez’s initial research project could have been dismissed as an irrelevant and minor anomaly. Instead, it led to a major theoretical innovation.
As I discovered by entering the field by decree rather than design, theoretical and empirical discoveries force us to acknowledge that we often know less than we think we do. Rather than heading too narrowly to what is already established, this example suggests that we have much to gain by being open to the unexpected and the unknown.
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Stathis N. Kalyvas is Gladstone Professor of Government at the Department of Politics and International Relations at University of Oxford.
PUBLICATION TO WHICH THIS FIELDWORK CONTRIBUTED:
• Kalyvas, Stathis N. The Logic of Violence in Civil War. New York: Cambridge University Press, 2006.
NOTES
1. Now a much easier option consists of getting a bridge type of visa and “serving” the two home years in small segments, mostly during summers.
2. Roger D. Petersen, Resistance and Rebellion: Lessons from Eastern Europe (Cambridge: Cambridge University Press, 2001).
3. James C. Scott, Weapons of the Weak: Everyday Forms of Peasant Resistance (New Haven, Conn.: Yale University Press, 2008); James C. Scott, Domination and the Arts of Resistance: Hidden Transcripts (New Haven, Conn.: Yale University Press, 2008).
4. David D. Laitin, Hegemony and Culture: Politics and Change Among the Yoruba (Chicago: University of Chicago Press, 1986); Diego Gambetta, The Sicilian Mafia: The Business of Private Protection (Cambridge, Mass.: Harvard University Press, 1996).
5. The limited research that existed at that time tended to privilege the highly ideologized experiences of activists rather than the experiences of ordinary people; e.g., Janet Hart, New Voices in the Nation: Women and the Greek Resistance, 1941–1964 (Ithaca, N.Y.: Cornell University Press, 2018).
6. Barrington Moore, Social Origins of Dictatorship and Democracy: Lord and Peasant in the Making of the Modern World (Boston, Mass.: Beacon Press, 2015); Theda Skocpol, States and Social Revolutions: A Comparative Analysis of France, Russia, and China (Cambridge: Cambridge University Press, 2015).
7. Stathis N. Kalyvas, “Wanton and Senseless?: The Logic of Massacres in Algeria,” Rationality and Society 11, no. 3 (August 1999): 243–85, https://doi.org/10.1177/104346399011003001. I considered conducting fieldwork in Algeria, but this proved impossible due to the situation on the ground in this country.
8. Thanks to the Harry Frank Guggenheim Foundation for their support!
9. Lars-Erik Cederman and Manuel Vogt, “Dynamics and Logics of Civil War,” Journal of Conflict Resolution 61, no. 9 (October 2017): 1992–2016, https://doi.org/10.1177/0022002717721385; Lars-Erik Cederman and Kristian Skrede Gleditsch, “Introduction to Special Issue on ‘Disaggregating Civil War,’ ” Journal of Conflict Resolution 53, no. 4 (2009): 487–95.
10. Stathis N. Kalyvas and Matthew Adam Kocher, “The Dynamics of Violence in Vietnam: An Analysis of the Hamlet Evaluation System (HES),” Journal of Peace Research 46, no. 3 (May 2009): 335–55, https://doi.org/10.1177/0022343309102656.
11. Elizabeth Kolbert, The Sixth Extinction: An Unnatural History (New York: Henry Holt, 2014), 70–91.