Justice and the Peace: A Time‐Sensitive Empirical Evaluation
Geoff Dancy Ph.D. candidate, University of Minnesota [email protected]
Eric Wiebelhaus-Brahm Instructor, Florida State University eric.brahm[email protected]
Paper Presented at the Annual Meeting of the International Studies Association, Montreal, Quebec, Canada, March 16-19, 2011.
Abstract: Prevalent in current discussions of peace-building are various claims about the ways in which justice-seeking mechanisms--like human rights trials and truth and reconciliation commissions— can quell violent conflict. In fact, ‘transitional justice’ has attained the status of orthodoxy among global peace-promoting actors and international institutions. Though propositions about the pacifying effects of transitional justice mechanisms have swirled about for over a decade, to date very few comprehensive studies have adequately evaluated them. In fact, many ‘realist’ scholars oriented toward producing political order remain justifiably skeptical regarding the impact of transitional justice institutions: what if they actually are destabilizing and cause a relapse into violent conflict? Furthermore, there has been little interaction between legalistic approaches emphasizing ‘unproven possibilities’ and scientific approaches emphasizing ‘empirical realities.’ More specifically, those deeply involved with transitional justice have rarely crossed paths with those enmeshed in conflict studies. We seek to address the lack of hypothesis-testing and dialogue by constructing an integrated model of peace transition, duration, and conflict recurrence that incorporates the newest information on cross-national transitional justice efforts. Utilizing the PRIO dataset, we test the proposition that domestic trials and truth commissions are more effective than political amnesties and repression for producing a lasting peace. Depending on the model chosen, we show that transitional justice mechanisms at worst have no effect, and at best slightly extend the duration of peace following violent conflict. Our findings encourage a reevaluation of the peace v. justice debate, one that moves toward more humility on each side.
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Introduction Even after more than twenty years, the so-called ‘peace versus justice’ debate remains at the center of the transitional justice field. When political violence comes to an end, warring factions, transitional governments, the international community, and civil society groups all weigh the possibility that attempts to address human rights violations during the conflict will reignite fighting. The global accountability movement’s most visible accomplishment, the International Criminal Court, performs its work under the banner of “Peace through Justice”. However, its actions in countries such as Sudan and Uganda have attracted criticism from a growing number of observers who see justice interventions as harmful to local peacebuilding initiatives. Despite efforts by the international human rights community to come to terms with its detractors through theoretical engagement (see Orentlicher 2007, 2010), it remains an open question as to whether or not justice efforts are destabilizing. The views of transitional justice supporters and detractors both rest on reasonable logic. Some argue that measures to address past human rights abuses may make peace more durable by righting wrongs, removing powerful perpetrators from positions of authority, and providing a deterrent against future acts of brutality. From this perspective, amnesties are an obstacle to achieving these goals. The lack of accountability inherent in amnesty laws may frustrate victimized populations and make them susceptible to bellicose rhetoric. By contrast, others argue that accountability measures may threaten peace and order. Fighters may be reluctant to lay down their weapons if threatened with punishment. The revelations of truth commissions may fuel renewed anger and accentuate intergroup divisions inimical to social cohesion. In this view, amnesties can exert a calming influence in fragile transitional periods and ultimately contribute to a more durable peace. Although both cause-effect relationships have some anecdotal support, we argue that broadly comparative empirics are needed. As Meernik et al. (2010) argue, “[r]igorous
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and empirical testing in the post-conflict environments of nations across time and space has only recently begun in earnest.” With this piece, we hope to contribute to this discussion. In this paper, we combine two different academic literatures that commonly speak past one another. The first is transitional justice, an interdisciplinary literature with strong legal-theoretic and sociological overtones (see Bell 2009). The second is peace science, a methods-heavy literature focused on econometric analysis of war onset, war termination, and peace duration (see Mason 2007). For better or worse, scholarly exchange between these subfields has been minimal, notwithstanding the fact that each is preoccupied with conflict resolution and peacebuilding. This resistance is very much an issue of professional and methodological taste. Both groups have been groping for answers. However, while legal interpretivists have been resistant to quantitative measures, econometricians have been disinclined to include justice-related variables in their models of civil war (see Thoms et al 2008, 2010; Dancy 2010).1 The opportunity for merging different approaches is ripe, and the payoff is potentially great. At stake are our baseline expectations for post-conflict justice, and a potential solution to the ongoing debate about the role of accountability in promoting peace. We weigh in on the controversy using a newly available longitudinal dataset.2 By assembling a month-by-month examination of 205 transitional peace spells over 40 years, our study presents the most comprehensive analysis to date in terms of data and method, and its findings uncover a great deal about the impact of various transitional justice mechanisms. In this paper, we begin by reviewing the findings of existing studies that examine the effect of transitional justice on the durability of peace. Second, we survey the civil war literature to highlight other factors previous studies have identified as important in explaining the persistence of peace. Third, 1
Exceptions include Lie, et al. (2007) and Meernik et al. (2010). This paper will present and critique each of those pieces. 2 This dataset is the product of work that authors have performed alongside research with Kathryn Sikkink and Leigh Payne at the University of Minnesota, sponsored by the National Science Foundation. Geoff Dancy is the NSF project director at Minnesota, while Eric Wiebelhaus-Brahm remains officially unaffiliated. While this specific dataset is the authors’ construction, all content related to trials has been produced in coordination with the research team at Minnesota, whom the authors would like to extend special thanks.
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we lay out our method of case selection and the propositions that we wish to test empirically. Fourth, we explain the model that we use to conduct our analysis. Fifth, we discuss our findings. Finally, we conclude by discussing the policy implications and suggestions for further research. Transitional Justice and Lasting Peace Given the fact that transitional justice mechanisms are designed to address histories of violence and repression, it is not surprising that they are viewed as important in shaping the prospects for long-term peace. Yet, there is disagreement over whether transitional justice is peace-promoting. Most in the legal theory camp believe that transitional justice increases the probability that violent conflict will not reemerge (Mani 2002; Elster 2004; Gloppen 2005). Generally speaking, engaging in transitional justice may boost a government’s legitimacy and dampen public support for social change through the use of force. The hypothesized means through which transitional justice contributes to peace, however, varies by mechanism. First, some argue that retributive measures can break cycles of violence through punishment, deterrence, or symbolic expression of the rule of law (Pankhurst 1999; Akhavan 2001, 2009; Elster 2004; Bass 2005; Kim and Sikkink 2010; for this three-part framework, see Drumbl 2007). Trials, for example, might reduce conflict by punishing those who were responsible for past violence. Theoretically, perpetrators’ willingness and ability to instigate further unrest may be hampered by their incarceration and/or a loss of support resulting from courtroom revelations. Second, truth commissions may prevent further conflict by recommending reforms that curb the excesses of security forces and by helping to promote reconciliation among former opponents. Third, trials and truth commissions both may placate victims’ desire for revenge by providing an acknowledgment of suffering and a sense of justice for past wrongs. Finally, transitional justice may play an educational role thereby limiting the ability of spoilers to upset the peace. Transitional justice processes attempt to produce an authoritative version of history that may
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individualize guilt and discredit institutions and causes that might otherwise foment renewed violence (Zalaquett 1995). Despite a wealth of claims in this vain, others from the political order camp contend that any peace-promoting properties of transitional justice are either nonexistent or better attributed to other features of transitional societies. In their view, the stabilizing effect of transitional justice is a result of wishful thinking, principled logics of appropriateness, or legal romanticism. Some argue that the prospect of transitional justice will keep soldiers on the battlefield, or will derail ongoing peace negotiations (Aron 1981; Huntington 1993; Fearon 2005; Branch 2007). Others conclude that transitional justice, trials and truth commissions in particular, raise tensions between targeted former repressive elements and new civilian leaders (Snyder and Vinjamuri 2003/2004; see also Long and Brecke 2003; Hadden 2004). Transitional societies often lack the capacity or the political will to conduct free and fair trials. As such, they may create martyrs or generate new grievances that could fuel renewed conflict. Amnesties may be essential in these environments to give fighters an incentive to lay down their arms, or “to encourage lower-level combatants to break rank” (Freeman 2009: 13; see also Cobban 2007 and Mallinder 2008). Where peace does persist in post-conflict settings in the absence of amnesties, many critics argue that transitional justice advocates mistakenly take credit when other factors are responsible. Focusing specifically on truth commissions, for example, Schiff (2002) contends that supporters are often quick to claim credit when tensions appear to subside. In particular, critics contend that transitional justice is not necessarily destabilizing only when conducted in well-established democracies or when amnesties have been enacted to insulate potential spoilers from punishment (Snyder and Vinjamuri 2003/4). However, for the most part, the claims from both sides of the controversy have not been subjected to adequate empirical scrutiny. Transitional justice proponents often make their assertions based upon normative grounds or impressionistic conclusions drawn from individual case studies. This has been a commonly repeated criticism of work in this emergent subfield
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(Mendeloff, 2004; Thoms et al, 2008, 2010). Two book volumes have examined assessments of transitional justice impact (Olsen et al, 2010; Chapman and ver de Merwe, 2009), and a September 2010 special issue of the International Journal of Transitional Justice pointedly confronts techniques of evaluation. A resounding theme is that even the most systematic pieces in the field leave much to be desired (see Thoms et al 2010). Snyder and Vinjamuri’s (2003) strongly critical judgments, for example, are based on a quick and superficial engagement with 32 individual cases. Similarly, Sikkink and Walling (2007) find a positive influence of trials on human rights and democracy in Latin America, but only by comparing broad averages of different standard measures over time. Finally, Olsen et al. (2010:129), in their study of the ‘peace dividend,’ present only a table with summary statistics linking different mechanisms to conflict recurrence—a strategy also employed by Dancy (2010). To date, few studies have employed statistical methods sophisticated enough to fully address the puzzle at hand: whether transitional justice mechanisms lead to a more or less durable peace. Two exceptions are Lie et al. (2007) and Meernik et al. (2010). Both studies are broadly cross-national, allowing the benefit of systematic testing of hypotheses across a large sample of countries, while controlling for the peace-promoting or peace-inhibiting effects of other variables identified by the qualitative and quantitative literature on civil war recurrence. Lie et al. (2007) provide the earliest example of systematic empirical research on the relationship between transitional justice and peace. They look at all civil war cases, defined by Uppsala-PRIO as a conflict with 25 or more annual battle-related deaths that occurred between 1946 and 2003. The study includes a broad range of transitional justice mechanisms from a dataset constructed by Binningsbø et al. (2005), namely trials, purges, reparations, truth commissions, amnesties, and exile. Lie et al. find that the way in which the conflict ended (victory or negotiated settlement), is most important in determining the duration of post-conflict peace. However, they find some support for the contention that transitional justice helps make peace more durable. Nonetheless,
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the effect of transitional justice is weak and inconsistent depending on the mode of conflict termination. This is particularly true of trials. Reparations and truth commissions, they conclude, are more consistently associated with prolonged peace. While an important first cut at the question, the study has some limitations. First, their findings with respect to transitional justice rarely approach conventional statistical significance even at a looser 90% confidence interval. Second, the dataset on which the study is based (Binningsbø et al. 2005) has not been publicly released so it is difficult to judge the validity of their conclusions. Relatedly, given that the dataset only goes through 2003, it is missing observations from more recent years. Finally, while the breadth of the dataset is generally an asset, this is of more limited use for their analysis. In general, the peace versus justice debate has focused on accountability-oriented transitional justice mechanisms like trials, truth commissions, and amnesties. Reparations programs have infrequently been part of these debates. Moreover, while their inclusion of exile is innovative and theoretically sound, transitional justice discussions rarely include exile as a mechanism. As a result of these differences, they may not be measuring transitional justice in the way that transitional justice defenders or critics do. Finally, while the authors are right to use duration analyses, they at times problematically impose temporal structure on their dataset when it is unnecessary. For example, they only examine periods of peace that follow a full two years of successful conflict termination, driving the number of failures down to a total of 16. We will discuss these and other methodological concerns below. More recently, Meernik et al. (2010) explore the impact of international tribunals and domestic trials--as coded by Kim and Sikkink (2008)--on the duration of peace. They also use Uppsala-PRIO’s civil war data to examine civil wars that ended between 1982 and 2007. They find no evidence that countries that experience domestic trials or international tribunals are more or less prone to renewed conflict. Even confining the sample to more democratic states, they find no
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evidence of a statistically significant relationship. It remains an untested possibility that renewed conflict might have been worse were trials or tribunals not utilized (Meernik et al. 2010: 322). Like the Lie et al. (2007) paper, this piece also has limitations. First, in contrast to Lie et al. (2007) or our analysis, they focus on only one type of transitional justice measure, trials. This limits the ability of researchers to draw conclusions about different accountability mechanisms instituted in conflict situations. Second, they are really studying the likelihood that any given country-year with a trial will coincide with a year in which a conflict breaks out (using probit analysis). In doing so, they treat all observations as completely independent, even if they are in the same country. Modeling when independent and dependent variable correspond without a consideration of transitional periods, timing, or context leaves out potentially crucial information. In an attempt to address these issues, the authors average scores on different variables across a five-year post-conflict period to move away from ‘yearly snapshots’ (325), but this method, by aggregating into even bigger chunks of time, drastically reduces the amount of information being considered in the model, artificially smoothing out variation. A final note about the empirical studies of transitional justice to date concerns sequencing and context. Though scholars of late have been emphasizing the order in which mechanisms are instituted (Fletcher et al 2009), and the holistic context into which they are planted (de Greiff and Guthie 2009), virtually no empirical studies provide leverage on these topics. For instance, we still do not know, on average, which mechanisms come first, nor do we know which order produces the best outcomes. Only by incorporating multiple mechanisms into one study and modeling time can one begin to address these concerns. In short, a time-sensitive approach is crucial. Even further, context is usually absent in large cross-national approaches. For instance, dense networks of amnesty laws (up to 16 in one case), multiple truth commissions of different duration, or various
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types of trials are all treated in the same way: they are coded as 1s in particular country-years. 3 Before elaborating how we address these concerns, we briefly review the literature on the durability of peace.
Factors Influencing the Durability of Peace There is a rich empirical literature on the causes of civil war onset and recurrence. In trying to determine the independent effect of transitional justice on peace duration, this literature provides a wealth of alternative explanations for which we should control. The way in which the previous fighting came to an end is an important factor. In addition, several studies have found that the nature of the previous conflict influences the likelihood that conflict will reemerge. Finally, characteristics of the society itself appear to have a significant influence on the durability of peace. Characteristics of the Previous Conflict The nature of the previous conflict plays an important role in the durability of the peace. Several studies have highlighted the importance of the scale of past violence. Some find that higher casualty rates reduce the risk of conflict resumption due to exhaustion (Hartzell et al. 2001). On the contrary, others argue that higher casualty figures may harden feelings and make opponents angrier (Doyle and Sambanis 2000; Walter 2004; Quinn et al 2007). In addition, the duration of the previous conflict appears to reduce the risk of reemergence as the sides become exhausted and less confident of victory (Mason & Fett 1996; Sambanis 2000; Fortna 2004; Walter 2004; Quinn et al. 2007). Research in the transitional justice field appears consistent with these findings on conflict duration. Comparatively short periods of conflict and repression seem more likely to incite demands for transitional justice (Barahona de Brito et al. 2001; Elster 2004). By
The Philippines has enacted 16 amnesty laws since 1970. Countries with multiple truth commission include Uganda, Chile, and South Korea. Types of trials include international, foreign, and domestic (see Sikkink, forthcoming).
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contrast, long, protracted conflicts make it harder to conduct transitional justice due to the difficulty of obtaining evidence, damage to judicial systems and other political institutions, competing resource demands, and war-weariness. What was being fought over also appears to be significant, although the literature has not generated consistent findings. Some studies find that identity conflicts are more likely to simmer and remain unresolved compared to conflicts fought over ideological differences (Rothchild & Groth 1995; Kaufmann 1996, 1998). Quinn et al. (2007), by contrast, find that ethnic revolutions are no more likely to reemerge. Other studies find that secessionist conflicts are more likely to reemerge because territory often remains not entirely under government control, which allows time for rebels to regroup (Walter 2004). Quinn et al. (2007), however, find secessionist conflicts are no more likely to reemerge than other types of conflict. More research is needed to resolve these controversies. Characteristics of Conflict Termination Several studies have found that the way in which the conflict ended is highly significant in determining whether conflict will reemerge. Generally speaking, negotiated settlements are less durable than a battlefield victory by one side of the conflict (Licklider 1995; Walter 1997; Hartzell and Hoddie 2003). Fortna (2004) also finds that victory reduces the risk of renewed conflict, but the relationship is less clear after the end of the Cold War. If the parties to the conflict put a halt to the fighting before one side defeats the others, they each will retain the capacity to resume the conflict in the future should they choose. Other research has found that transitional justice is more likely, and is more likely to be retributive in nature, when the balance of forces between the ancien regime and its opponents is more unequal (Barahona de Brito et al. 2001; Binningsbø et al. 2005). At the same time, Hartzell and colleagues find that negotiated settlements that result in powersharing arrangements are more durable and longer lasting (Hartzell 1999; Hartzell and Hoddie 2003; Hartzell, Hoddie, and Rothchild 2001). Moreover, some research suggests that government
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victory is less stable than rebel victory because the rebels’ original grievances are unlikely to be addressed in such a scenario. In addition, the rebels can more easily hide and reconstitute themselves following defeat. All else equal, third party support for settlements appears to make them more durable (Walter 1999; Fortna 2004; Doyle and Sambanis 2000). Structural Features of the Polity Characteristics of the country itself matter. Conflict is less likely to reemerge the more democratic the post-conflict government is (Hartzell et al. 2001; Hegre et al. 2001; Walter 2004; Quinn et al. 2007). Some transitional justice scholars also contend that transitional justice measures are likely to be more effective in more democratic societies (Barahona de Brito et al. 2001; Mendeloff 2004). Walter (2004) contends that the relationship between regime type and conflict recurrence is nonlinear. Rather, she finds that both clear democracies and autocracies are at less risk of conflict resumption. Rather, semi-democratic states are at the greatest risk. In addition, studies typically find that more economically developed countries are at reduced risk of conflict resumption (Fortna 2004; Walter 2004; Quinn et al. 2007). In wealthier societies, potential combatants have more to lose from fighting. Moreover, governments are better able to invest in infrastructure and social programs to dampen dissent. Finally, population size may be significant. Some studies find that states with larger populations are at greater risk of conflict resumption because rebels have a larger pool of potential recruits (Fearon and Laitin 2003; Sambanis 2004). Quinn et al. (2007), however, find to the contrary that larger populations are associated with lower risk of conflict resumption. Toward a Synthesis While it is commonplace to assume that macro-social outcomes of transitional processes hinge on the “choices successor elites make in dealing with the past” (Huyse 1995:51), it is also clear from the peace science literature discussed here that clever policy decisions alone are not enough to ensure a durable peace. The structure in which certain decisions are made must also be
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accounted for. To paraphrase Marx, leaders make their own peace, but they do not make it just as they please. This tension between structure and agency in transitional moments, we argue, is the crux of the debate between so-called ‘realists’ and ‘legalists.’ Whereas realists tend to understand social outcomes to be mostly a function of slow-changing structural configurations, in line with the early generation of studies of order and political change (see Huntington 1968), legalists tend to emphasize the progressive change that can be fomented through the establishment of, and adherence to, new and better rule-based practices. On the one hand, immersed in the peace science literature, one might come away with a realist sense of resignation, an inclination to ask the question “what can be done?” If the creation of a more sustainable peace means eliminating economic imbalances or satisfying separatist grievances, both sticky factors, then policy choices in the short-term are hard to come by. On the other hand, immersed in the transitional justice literature, one might be fooled into thinking that options are limitless, or in turn be immobilized by the dizzying array of ambitious short-term propositions. For every theoretical or empirical claim concerning the beneficial social potential of a transitional justice accountability mechanism, there is a counterclaim cautioning of the dangers of unintended consequences. Together, these make for boundless, ungrounded policy thinking. Hence the persistent call for better empirics and baseline expectations. We endeavor to answer this call with the soundest method we can muster, and to do so while bringing along as little theoretical baggage as possible. First, we do not privilege any particular transitional justice accountability measure. Second, we conduct our empirical tests with ‘flat priors,’ so to speak. What this means is that we do not make hypotheses about the causal or directional effects of any particular variable. In effect, we are conducting a host of two-tailed tests, obviating the need for an extensive presentation of hypotheses.4 Third, much like those who conduct Bayesian analyses, we
This has the added benefit of allowing us not to reject as wholly insignificant those variables that have a strong effect but in the opposite direction to that expected.
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intend to learn directly from the data, rather than imposing deductive, theory-laden assumptions on the dataset we have collected.5 The next section elucidates the method we use for creating models that integrate the assertions of the peace science and transitional justice literatures.
Case Selection and Variables Case Selection The purpose of this study is to uncover the effects of transitional justice mechanisms on the duration of peace. To conduct any empirical test, a methodologically sound sample must be selected. However, when dealing with issues of transitional justice, case selection is a thorny issue. The reason is that the concept of transition is an intellectual construct less settled than others like state, economy, or year. A transition can only be labeled as such post-hoc. Moreover, embedded in the subfield are ambiguities over what “a state is supposed to be transitioning to” (Leebaw 2008:101). While some authors look specifically at countries transitioning to consolidated democracy (Kritz 1995, Teitel 2000, Kim and Sikkink 2010), others examine only those that have recently experienced violent conflict or atrocity (Bassiouni 2002, Meernik et al. 2010). Still others inadvertently choose to analyze some combination of both types of cases (Snyder and Vinjamuri 2003/4, Backer 2009).6 In fact, “just about every comparative assessment of transitional justice effects examines a different universe of cases” (Dancy 2011). Our way to address this problem is to lean toward inclusion, and to avoid throwing out cases that do not fit a particular mold. First, we identify and include all peace spells that followed either a democratic transition or a conflict termination.7 A peace spell is a period of time within a country in which 25 or fewer
Of course, it is impossible to completely remove theory from the process of dataset construction, primarily because many difficult decisions must be made along the way. However, we do our best both to explain these decisions and to attempt various codings, operationalizations, and model implementations. We borrow the term ‘theory-laden’ from John Freeman, who uses it in his lectures on time series analysis. 6 Some, like Backer (2009), even look at cases that are generally considered neither democratic or conflict transitions. 7 “Democratic transition” is defined as either of two phenomena based on Polity IV data: state formation into a democratic polity (ex. Bosnia) or a 3-point increase on the Polity II scale in a given year. “Post-conflict transition” is
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total battle deaths per year occur as a result of internal or internationalized internal conflict (Gleditsch et al 2002).8 The justification for observing peace spells in both democratic and conflict transitions is that scholarship predicts potentially adverse effects for accountability mechanisms on sustainable peace in either instance. In other words, for us the presence of a previous conflict is not a sufficient condition for the onset of a new conflict because democratic change might also usher in violence, especially if all actors do not accept democracy as the only game in town.
Additionally, selecting cases in this way allows us to test for the effects of
transitional justice on the duration of peace spells following only democratic transitions, following only post-conflict transitions, or following both simultaneously. Second, we choose to examine the period 1970-2009. Starting our sample in 1970 allows us to capture the period shortly before the beginning of the third wave of democratization while also allowing us to avoid including decades of observations where human rights-related policies would not have been pursued because such policies were not yet practiced.9 Third, unconventionally, we measure our dependent variable, peace spell duration, in months rather than years. One reason for this choice is that most of the data on which we construct our variables is recorded by month, and sometimes even by day. The second reason is that aggregating to the year level obscures extremely important monthly variation. For instance, in most analyses, the period of peace between the Arusha Accords in August 1993 and the onset of the Rwandan genocide in April 1994 would be ignored because there were at least 25 battle-related deaths from conflict in each year. However, in our analysis, this would be a peace spell of seven months followed by a peace failure. One final reason for this decision is that, as a general rule,
any period following the termination of conflict involving state forces that reached 25 total battle deaths on the PRIO scale (see Gleditsch et al, 2002). We rely on the definition by the UCDP/PRIO Armed Conflict Project, which defines a conflict as “a contested incompatibility that concerns government and/or territory where the use of armed force between two parties, of which at least one is the government of a state, results in at least 25 battle-related deaths” (See UCDP codebook). 9 We are aware of issues caused by left-truncated data, though left-truncated is the norm in social science rather than the exception. Still, we include variables that help us model the stock of factors that different cases inherit from leftcensored periods. 8
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temporal aggregation, as opposed to fine-grained disaggregation, is a recipe for losing valuable information and weakening the robustness of statistical findings (see Freeman 1989). Furthermore, we impose no time limits on a spell for it to count. Whereas Lie et al. (2007) only include peace spells that last for at least two years, we treat any period of peace as significant.
Independent Variables Following the literatures we reviewed above, we split 21 potentially influential independent variables into four groups, which we order by sequential relevance. Group 1 includes characteristics of the previous conflict, and Group 2 includes characteristics of the conflict’s termination. These first two groups, because they precede the beginning of each peace spell, remain static over the duration of the peace spell. For this reason, they do not vary with time (i.e. they are not ‘time-varying covariates’). For example, if a violent conflict ended with a government victory, the following peace spell would be coded “1” for its entire duration. This type of coding is theoretically justified by the voluminous amount of work that highlights the path-forming nature of peace settlements and the balance of forces at the transition. For the variables in these groups, we use straightforward operationalizations that follow convention practice (See Table 1). However, one variable that requires some additional explication is ‘Risk Set’. We utilize this variable to capture the patterns of conflict and peace in each country over time. Risk Set is used to delineate how many previous transitional peace spells a country has experienced. The first post-conflict or democratic transition peace spell that a country undergoes during the 1970-2009 period is scored as “1” during the duration of the spell. If a conflict recurs, then ends, the following peace spell is coded as “2”, and so on down the line. In our sample, the highest number for Risk Set is 6 for Senegal. That is, five times Senegal experienced a violent conflict that ended and was followed by a peace spell. We utilize Risk Set to control for the relative proneness of some countries to be serially conflictual.
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In our model, Groups 3 and 4 include time-varying covariates (TVCs), meaning that their value can change in the midst of a peace spell. Group 3 incorporates variables measuring the stock of accountability mechanisms in the country over time, and Group 4 includes structural features of the polity. Groups 4, like Groups 1 and 2, uses standard measures to describe different characteristics of the country. Group 3 includes the variables that capture the effects of accountability mechanisms. Below, we provide a more in-depth explanation of how we operationalize these variables. a. Amnesties The first variable is cumulative number of amnesty laws that a country has enacted in the sample period. Mark Freeman (2009:13) defines an amnesty law as an “extraordinary legal measure whose primary function is to remove the prospect and consequences of criminal liability for designated individuals or classes of persons in respect of designated types of offenses irrespective of whether the persons concerned have been tried for such offenses in a court of law.” Louise Mallinder’s Amnesty Law Database catalogues such laws (274 laws are included in our dataset) down to the day of passage. While amnesties differ widely in their intention, their target, and the crimes that they excuse, we group them together because any amnesty, we believe, generally seeks to serve as a safety valve for grievances that could fester and lead to conflict activity on the part of peace spoilers (on spoilers, see Stedman 1997). Again, while some would predict that carefully timed amnesty laws could assuage the impulse to keep fighting, others see amnesty laws as an unnecessary legal barrier to demands for retribution. In short, amnesties could feasibly have either a positive, calming effect, or a negative, frustration-inducing effect. Regardless, we might comfortably assume that the more such laws that exist on the books, the greater the magnitude of whichever effect is present. b. Truth Commissions The second variable is cumulative years of truth commission operations. A truth commission
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is a newly established and temporary commission officially sanctioned by the state, whose mandate includes investigative powers, which at some point operated to investigate a pattern of abuses to personal integrity rights that occurred over a period of time, some which were perpetrated by state actors” (adapted from Dancy, et al. 2010). Truth commissions have lasted as long as 11 years, though the average is closer to 1.5 years. For every truth commission in the world, we document the month in which it started operating, and the month in which it ceased operations. For each addition year of operation, our variable was scored one point higher (rounding up for each period over 6 months). Some suspect that truth commissions, by providing victims with information and official recognition, serve as a salve for a restless society emerging from an abusive period. Others think that truth commissions simply provide a bandaid for wounds left in the body politic, leaving them to fester in the future. Either way, truth commissions that last longer are more likely to have an impact because they have more time to accomplish their tasks, they attract more attention, and they become more socially resonant. c. Domestic Trials Most studies of transitional justice do not sufficiently separate out different trial-related phenomena. Following Sikkink (2011), we include three different types of trials—domestic, international, and foreign. Unlike some other studies, we place strict criteria on what qualifies a trial as an accountability mechanism. For example, Lie et al. (2007) count any trials that followed a conflict transition. Olsen et al. (2010) count all high-profile court verdicts that followed democratic transition. Each of these studies falters by including trials that might not use fair procedures, that are not necessarily related to human rights crimes, and that might consist of show trials for political crimes. By contrast, Kim and Sikkink (2010) only count human rights-related domestic judicial activity in a county, and do so even if it did not produce a verdict.10 We find this
The authors write, “To be included in the data set, the prosecution activity discussed in the report must inflict costs on a government agent accused of having individual criminal responsibility for human rights violations. Some of our
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to be a useful approach to follow. As realists would have it, domestic trials risk not only overburdening already over-taxed judiciaries (Cobban 2007), but also stirring up trouble with those holdover elements from the previous conflict who do not want to be targeted by a transitional regime. Legal supporters would reply that domestic trials strengthen the rule of law, potentially reviving a dormant judicial branch of government (Smulovitz 2002), and interrupt conflict patterns by targeting those responsible for instigating mass violence.
Like the other mechanisms, we
expect more domestic trial activity to have a more pronounced effect on the durability of peace over time. d. International trials Though scholars usually support or attack trials in the abstract, much of the debate really centers on the role of international courts—both ad-hoc tribunals and the International Criminal Court. International courts are lightning rods for criticism because they represent starkly outside, ‘Western’ intervention into the affairs of sovereign states and cultures. Some see such interventions as not only neo-imperial, but meddlesome and counter-productive because they halt naturally unfolding peace processes (Tully 2005; Turner 2008; Subotić 2009; Branch 2007; Fiss 2009). Others argue that positive, though incremental, changes have been ushered in through the operation of such courts, which have inspired moves toward victim satisfaction in the former Yugoslavia (Nettelfield 2010; Orentlicher 2010) and peace in African states (Akhavan 2009). In cross-national empirical research, only two studies have even begun to incorporate international trials into empirical studies. Whereas Meernik et al. (2010) observe only those countries subject to ad-hoc court jurisdiction (the former Yugoslavia, Rwanda, Sierra Leone, East Timor, and Indonesia). Kim and Sikkink (2010) include these plus Cambodia and those countries that have trials involve former heads of state and high-level officials, but trials of lower level officials including police officers and prison guards are also included. Prosecutions can be initiated either by governments themselves or by individuals or groups. In common law countries, only governments initiate criminal prosecutions, but in some civil law systems, victims and groups representing victims acting as ‘private prosecutors’ may initiate criminal proceedings either directly or indirectly” (Kim and Sikkink 2010:248).
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been investigated by the International Criminal Court—Uganda, the Sudan, the DRC, and Kenya. We follow the latter strategy, and as with the other justice-related variables, we count up for every year that a country is subject to internationalized trial proceedings. e. Foreign Trials A final type of judicial activity that we include in our analysis is prosecution through foreign trials, which involve one state’s efforts to prosecute citizens of another state under international human rights treaty law. Universal jurisdiction is often confused with the officially authorized jurisdiction of international courts, but it is a fundamentally distinct process. Few have endeavored to document all uses of universal jurisdiction, but we include up to 18 different countries whose citizens have been tried by foreign courts. Where Kim and Sikkink (2010) lump these together with international trials, we keep them separate in order to observe any unique impacts associated with foreign trials specifically. One of the most influential books written on transitional justice, The Pinochet Effect, concerns the way in which a universal jurisdiction case initiated by Spain against Augusto Pinochet jump-started judicial activity in Chile (Roht-Arriaza 2005). Left unaddressed is how foreign trials might influence peace. One possibility is that foreign trials could indict human rights abusers in the midst of intractable conflict, or during times when it is unlikely that domestic courts will have the capital or the inclination to do so themselves. On the other hand, Goldsmith and Krasner (2003:51) argue, with little substantiation, that ‘‘a universal jurisdiction prosecution may cause more harm than the original crime it purports to address.’’ We weigh in on this debate by considering the independent effect of foreign trials on the duration of peace spells.
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Table 1. Variables Groups with Descriptions and Source Information 1 Group 1: 2 Characteristics 3 of Previous 4 Conflict 5 6 7 Group 2: 8 Characteristics 9 of Conflict 10 Termination 11 12
Variable Name Duration of Conflict Government Conflict Territorial Conflict Maximum Number of Conflicts Maximum Intensity Risk Set Government Victory Rebel Victory Ceasefire Agreement Cessation through Low Conflict Peace Agreement UN Peacekeeping Operation
13 Cumulative Amnesty Laws
Explanation A count of the total months that the preceding conflict lasted from beginnging to end Whether the prior conflict was fought over the political system or government rule Whether the prior conflict was fought over terrorial or secessionist aims The maximum number of armed oppositions fighting during the previous conflict period The maximum fighting intensity reached during the previous conflict period (0-2) A marker indicating how many previous at-risk peace spells have existed in the country Whether the conflict ended with a government victory Whether the conflict ended with a rebel victory Whether the conflict was terminated by a ceasefire
16 Cumulative International Trial Years
17 Cumulative Foreign Trial years Group 4: Structural Features
18 19 20 21
Regime Type Regime Type Squared Total Population (logged) GDP per capita (logged)
Whether the conflict ended simply through the cessation of conflict Whether it was ended by a peace agreement Whether the spell featured a UN Peacekeeping Operation
How many amnesty laws the country had in the sample time period. Counts upward and Mallinder's Amnesty sustains score for each additional law. Law Database
How many years of truth commission operation the country had in the sample period 14 Cumulative Truth Commission Years following the first operating month. Counts upward and sustains for each additional truth commission year. Group 3: 15 Cumulative Domestic Trial Years Stock of Accountability
Dancy et al (2010); Hayner (2010)
How many years of domestic trials the country had in the sample period following the first operating month. Counts upward and sustains for each additional domestic trial year. How many years of international trials to which the country was subject in the sample period following the first operating month. Counts upward and sustains for each additional international trial year. How many years of foreign trials to which the country was subject in the sample period following the first operating month. Counts upward and sustains for each additional foreign trial year. Polity II 20-point regime-type index Polity II 20-point regime-type index squared The log of the country's total population The country's wealth measured in GDP per capita (2000 US Dollars), logged
AHRC/NSF Transitional Justice Database Project
Polity IV World Bank Databank
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A Note on the Coding of Transitional Justice Variables Before we move onto the presentation of method and our findings, we issue a note about the choice to include cumulative year scores for each of the mechanisms, a technique we refer to as sustained coding. To illustrate the nature of the coding scheme, we look first at Chile. Because Chile has had the most domestic trials for former junta members, it has the largest number of trial years—19—by 2009. What this means is that since its first trial in 1991, Chile has had at least one trial in 19 different years.11 We know from Collins’ (2010) extensive data collection project that the raw number of domestic trials is actually much higher. In terms of coding, this variable counts upward as the country experiences more trials; each new year with a trial, the number increases by one unit for all following months. The same cumulative coding rule applies for number of truth commission years and number of amnesty laws.12 An additional feature of the coding for these variables is that after activity stops, each following month is still coded that number until activity resumes or the last month of the dataset, December of 2009, is reached.13 The somewhat unorthodox coding scheme used for these variables is theoretically necessary for a few reasons. First, because these institutional mechanisms are arguably more effective when they are given time and resources to function properly, a larger number of years of operation indicates deeper institutionalization and a more thorough fulfillment of the mechanism’s mandate. Therefore, cumulative coding is needed to capture the varying degrees to 11
We use ‘years’ because we do not have a raw count of actual trials, and counting up by each month following initial trial activity would artificially inflate the magnitude 12 The only difference here is that amnesty laws themselves, not the duration of amnesty laws, is counted. To date, no data exists on the duration of such laws. Because they are legal enactments, we treat them as if they have a lasting effect throughout the period following their passage. 13 The only drawback to this method is that it creates what we refer to as the ‘straddler problem.’ Because variables with sustained coding can roll over from one peace spell to a following conflict spell, then onto another peace spell, it means that the effect of the mechanism straddles different transitional periods. This problem is most pronounced for truth commissions, which are temporary bodies that do not continue to operate in the future, as trials and amnesties do. There are only five straddlers. Two, Central African Republic and Uganda ’86, are coded across multiple spells, where Haiti, Nepal, and Nigeria inherit truth commissions from previous conflict periods. We test the effects of alternate coding for truth commissions in Model 5.
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which a transitional justice mechanism has been socially embedded. Second, like realist studies that emphasize the path-dependent nature of former policies or structural configurations, we suppose that these institutions have cachet, leaving a legacy that continues to exert an effect over time. This is why we label this group ‘stock variables.’14
If sustained scoring was not used, the
combined, additive effects of accountability mechanisms over time would be ignored. Third, methodologically speaking, sustained coding heavily weights those cases in which more trialyears have been observed, which is appropriate given that those cases are by all accounts the ones that have the highest raw number of trials. In short, the number of trial years is a good proxy for the total number of trials. Now that our coding decisions have been explained, we turn to a presentation of our findings, which are various and, at times, surprising. We first discuss two hot-button issues—context and sequencing—and then proceed to a detailed exploration of our empirical findings.
Findings Context and Sequencing One regrettable thing about complex statistical presentations is that they typically leave out useful descriptive summaries that address long-standing questions. For example, in what context are different mechanisms most likely to be instituted?
Table 2 shows summaries of
each accountability mechanism across country contexts. We observe the country-month in which each type of mechanism was established. For amnesties, we count every single law that was passed. For truth commissions and trials, we count only the first instance of each. The columns represent the various contexts in which the five different mechanisms are set up. What
John Gerring et al. (2005), in a related fashion, argue that democracy should be coded as a stock variable, meaning that its scores should accumulate over time.
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ultimately emerges is a fairly diverse spread. Generally speaking, though, a few patterns are visible. First, all of the mechanisms are more prevalent in peace spells following negotiated settlements, and least likely after rebel victories. (The only exception is amnesty laws, which are most likely to follow government victories in internal conflict.) This finding we might expect because issues of how to reckon with former abuses commonly arise during unfolding processes of negotiation between previously warring parties. Second, all of the mechanisms are more common to peace spells following democratic transitions, but roughly half are initiated during non-democratizing peace spells or during resumed conflict periods. Unexpectedly, Table 2 demonstrates how much is missed when only democratic transitions are studied. It also suggests that modeling strategies should take into account the potential for peace durability to differ with peace spell context.
Table 2. Context in which Accountability Mechanisms are Instituted15
Peace Government Agreement Victory Amnesty Law Truth Commission Domestic Trial International Trial Foreign Trial
28 (16)* 7 7 2 6
38 (21) 7 3 1 3
Rebel Victory 13 (9) 4 2 1 1
Peace Spell Peace spell with without Resumed democratic democratic Conflict** transition transition 101 (48) 25 (23) 35 3 11
68 (38) 6 (5) 21 4 4
108 (35) 6 8 3 3
* The first figure is the raw total, and the figure in parentheses is total number of country cases **Because the paper is about peace spells, mechanisms in this column, which occur during resumed conflict spells, are excluded from the statistical analyses.
“After” means that the mechanisms followed the categorized type of conflict resolution. “During” means that the mechanism was using in the midst of the categorized
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Beyond context, a second question is, in what order are these mechanisms normally established? Table 3 presents cross-national data on the number of months into peace spells, on average, when each mechanism is adopted. For all cases, international intervention has the lowest average score, meaning that it is most likely to happen first in any given context. This is not surprising given that the international community moved quickly to address crimes against humanity in Rwanda and the former Yugoslavia after the fighting was finished. Overall, amnesties and domestic trials have initiation times that are very close—within a year of one another. On average, they are both instituted around five to six years into peace spells. This relationship holds irrespective of context. Tellingly, amnesties always precede trials, which
Table 3. Average months into peace spells until the first instance of each mechanism
In democratizing peace spells
In nondemocratizing peace spells
gives us some leverage on the question of typical sequencing. While some have speculated that recent increases in the number of amnesties represent a broad effort to counter the justice cascade (Olsen et al. 2010), Kathryn Sikkink (2011) has consistently argued that trials in fact are
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a response to impunity-protecting amnesties. Our data hint that the latter account appears more accurate. Our findings also may indicate that trial activity was enabled only through the stability produced by an amnesty. However, this seems less likely. Because amnesties are not typically enacted until a full five years into a peace spell, it does not stand to reason that they are part of a first response to conflict resolution. Amnesties, like justice mechanisms, do not enter the transitional equation until years after the onset of peace. Truth commissions, it is evident, are comparatively slow to develop. The average timing of a truth commission is over eight years into peace spells. In some ways, this should make us skeptical of the conventional wisdom that truth commissions are primarily used as a delay tactic to divert attention away from other forms of justice. Of course, we would hesitate to make grand conclusions based on these data, which are patterns without trends. These are basic averages across a number of cases and over several decades. The only way to satisfactorily address issues of sequencing is to create case-by-case timelines. That does not mean, however, that time cannot be precisely modeled within analyses of transitional justice impact. That is a task, we argue, for which hazard models are uniquely suited. Duration Analysis The dependent variable for our analysis is the duration of peace in months. From our dataset, we isolate 205 peace spells (across 117 countries) that have followed either the termination of a previous internal war or the beginning of a democratic transition (See Figure 1). Because we are interested in observing the length of time a peace spell ‘survives’ without violence again erupting, we employ event history methods (aka. duration analysis), which allows us to model not only if the peace spell ‘fails’ but also when it fails (See Figure 1 for survival estimates over time). Like Lie et al. (2007), we estimate the influence of our four groups of
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independent covariates on peace spell failure rates using a Cox proportional hazard model.16 We treat each peace spell as a single event that either ends with the resumption of conflict (failure) or December 2009, the last month in our dataset.17 The latter are ‘right-censored’ observations, which are accounted for in the likelihood function (see Box-Steffensmeier and Jones 2004). Positive coefficients in our model indicate that the covariate increases the log hazard rate, i.e. a unit increase in the independent variable makes a recurrence of conflict more likely. Conversely, a negative coefficient means that the hazard rate is falling with an upward change in the covariate. Finally, both quantitative and qualitative work on transitional justice has presumed that there are strong regional effects on both the choice to institute accountability mechanisms and on the outcomes that they produce (e.g. Clark 2010, Olsen et al. 2010, Kim and Sikkink 2010). For this reason, we estimate our models clustering by region, and we report adjusted, robust standard errors. Figure 1. Description of peace spell data and charted survival estimate
Kaplan-Meier survival estimate
Peace Spells 205 Number of Countries 117 Total months at risk 25,758 Median # of months at risk 80 Mean # of months at risk 127 Minimum # of months at risk 2 Maximum # of months at risk 463 Conflict Failures 112
200 300 analysis time
Cox models are semi-non-parametric, meaning that they allow the modeler to make fewer assumptions about the distribution of failure times or the baseline failure rate (see Box-Steffensmeier and Jones 2004). The use of single events brings with it the problematic assumption that various peace spells in the same country are independent of one another. We would prefer to use repeated events using conditional risk analysis to account for this. However, because peace spells do not directly follow one another in time—due to the presence of interim conflict periods—this mode of analysis is unusable. We control for the effects of multiple spells per country by including the risk set variable, which identifies those spells that are repeated events within our sample. We also include variables that are unique to the country over time.
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Table 5. Cox proportional Hazard Models Results with Coefficients and Robust Standard Errors
Duration of Conflict Government Conflict Territorial Conflict Maximum Number of Conflicts Maximum Intensity Risk Set Government Victory Rebel Victory Ceasefire Agreement Cessation through Low Conflict Peace Agreement UN Peacekeeping Operation Cumulative Amnesty Laws Cumulative Truth Commission Years Cumulative Domestic Trial Years Cumulative International Trial Years Cumulative Foreign Trial years Polity 2 Polity 2 Squared Log Population Log GDP per capita Number of subjects Number of failures Time at Risk Log Likelihood
Mode l 1
Mode l 3
Mode l 4
Mode l 5
Full model without GDP or population
Model 2 in democratic transitions
Model 2 in peace spells without democratization
Model 2 with different TC variable
-0.003 (0.002) -0.069 (0.179) 0.468** (0.205) 0.555*** (0.150) 0.410** (0.161) -0.128* (0.068) -1.016** (0.468) -0.002 (0.351) -0.375 (0.342) 0.436* (0.076) -0.491* (0.278) 0.168 (0.212) 0.133*** (0.034) 0.154*** (0.019) -0.145** (0.058) -0.109 (0.089) 0.195 (0.400) -0.036** (0.019)
-0.008* (0.005) -0.116 (0.335) 0.938*** (0.336) 0.930** (0.407) 0.773 (0.824) -0.197*** (0.076) -2.232*** (0.719) -1.401** (0.562) -0.958** (0.469) -0.135 (0.720) -0.565 (0.812) -0.007 (0.240) 0.100 (0.064) 0.150*** (0.042) -0.247*** (0.068) -0.342** (0.154) 0.262*** 0.070 -0.139*** (0.024)
-0.002 (0.003) 0.734* (0.394) 0.796*** (0.280) 0.471* (0.268) 0.476* (0.269) -0.725*** (0.115) -0.832** 0.424 0.302 (0.518) 0.150 (0.283) 0.736** (0.320) -0.706 (0.902) 0.597* (0.355) 0.361*** (0.064) 0.299 (0.239) -0.306 (0.408) -0.012 (0.242) -0.041 (0.840) 0.037 (0.031) -0.009* (0.005)
-0.003 (0.002) -0.082 (0.182) 0.442** (0.196) 0.527*** 0.155 0.424*** (0.162) -0.090 (0.067) -1.003** (0.434) 0.040 (0.327) -0.441 (0.343) 0.420** 0.239 -0.441 (0.272) 0.160 (0.203) 0.126*** 0.034 -0.534 (0.326) -0.123*** (0.043) -0.102 (0.094) 0.177 (0.414) -0.032* (0.018) -0.013 (0.003)
204 112 25495 -498.485
115 50 15283 -180.428
105 62 10212 -225.692
204 112 25495 -499.433
-0.005* (0.003) -0.198 (0.195) 0.263 (0.306) 0.626*** (0.193) 0.368** (0.168) -0.125 (0.089) -1.181** (0.601) -.0029 (0.263) -0.286 (0.403) 0.541* (0.298) -0.392 (0.305) 0.140 (0.280) 0.114*** (0.043) 0.105*** (0.040) -0.106** (0.056) -0.068 (0.117) -0.116 (0.449) -0.020 (0.018) -0.009** (0.003) 0.167** (0.069) -0.242* (0.132) 186 95 23240 -411.398
*p > 0.10 ** p > 0.05 *** p > 0.01
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Table 5 reports the results of five models we specified to integrate factors from the transitional justice and peace science literatures. Model 1 includes all 21 variables described above. Of those characteristics of the previous conflict (Group 1), we see that only the maximum number of conflicts and maximum intensity are statistically significant; what the conflict was fought over (government or territory) does not prove influential. In other words, if state forces previously had to war against more than one armed group simultaneously, then whatever peace is established is more likely to break down. Each additional previous conflict increased the likelihood of failure by 62.5%. Moreover, for each additional level of fighting intensity in the previous conflict period, the failure rate increased by 36.8%. In short, higher frequency and greater intensity of previous fighting made for unsettled peace spells, though the length of the conflict and the nature of the grievance did not. Of those characteristics of conflict termination (Group 2), only government victory effects the duration of following peace spells, and it does so in highly significant fashion. Peace spells following government victories were approximately 1.2 times less likely to revert to violent conflict in the future. The transitional justice stock variables (Group 3) perform surprisingly well in the model, proving to have both substantively and statistically significant effects. There is little evidence to indicate that either international or foreign trials alter the course of peace spells, perhaps because there are so few of each type. However, amnesty laws, truth commissions, and domestic trials all prove influential. For every additional amnesty law that a country has passed, the risk of conflict recurrence increases by 11.4%. That is, contrary to many claims that amnesties are orderpromoting, on average they seem to do little to assuage the impulse to take up arms.18 Truth commissions, perhaps most surprisingly, have almost the exact same effect as amnesty laws. For
Our interpretation here is still speculative because we have not done enough to distinguish between different types of amnesties. This is a future direction in which we hope to take the research (see conclusion).
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every additional year that a truth commission operates in a country, the survival time for peace decreases by around 10.5%. This provides some validation to those skeptics who have stringently critiqued the ‘baseless’ empirical assumptions that inform the truth-telling-asreconciliation model (e.g. Mendeloff 2004). Finally, domestic trials appear to exert an effect opposite to that of amnesties and truth commissions. For every additional trial year a government produces, the risk of conflict recurrence decreases by 10.6%. Taken together, these results suggest that, in line with weaker findings produced by Lie et al. (2007), retributive modes of justice are more effective for resolving conflict, whereas truth-telling and legal immunity are more likely to exacerbate tensions. Finally, variables measuring structural features of the polity also achieve significance. The squared measure of regime type (Polity2) is statistically significant and negative. This indicates that both strong autocracies and strong democracies are at lower risk of conflict resumption. For every unit increase in the squared term, which can reach as high as 100, the failure rate decreases by 0.9%. A country’s total population also seems to make a difference. The larger the population, the more likely a peace spell is to break down. The presence of more people creates more opportunities for grievances to (re)emerge. GDP per capita, while close to the conventional .05 benchmark for significance, falls short. However, the direction indicates that, if anything, wealth bolsters the duration of peace. While Model 1 performs very well, and does not violate the proportional hazard assumption,19 we still have qualms about the full specification. The reason is that 18 peace spells are dropped because of missing GDP and population data from the World Bank. As a corrective, we exclude these variables and re-run the analysis to produce the results listed under Model 2.
We tested this using a global chi-square test, which was statistically insignificant (p-value = 0.254), indicating that the hazard assumption holds.
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As is evident from Table 5, the model produces similar results to Model 1--with minor changes in magnitude for the variables of interest—except that two additional variables become significant. The first is territorial conflict, and the second is the Polity 2 measure. One might suppose from this that democracy and territorial grievance are in some ways a function of wealth and population, which is not far-fetched. But because we are able to model more information by excluding the latter, we prefer Model 2 to Model 1. Models 3 and 4 use the same variables as Model 2, but they focus on a subset of cases based on the nature of the political transition. Model 3 is run only on those peace spells following democratic transitions (including those that are simultaneously post-conflict). By contrast, Model 4 is run only on those peace spells where democratic institutionalization is not taking place. We do this to observe the effect of the variables in disparate transitional contexts. In Model 3, the intensity of previous fighting drops out, as do amnesty laws. This indicates that in those countries transitioning into more democratic forms of governance, the extremity of previous violence and the presence of laws guaranteeing impunity no longer incite conflict, perhaps because those with nagging grievances have other avenues for political participation or conflict resolution. Such speculation is supported when we compare the findings to Model 4, wherein amnesty laws again become salient and negative, increasing the failure rate by 36% per law. What this means is that peace spells in countries where democracy is absent or not formally institutionalized are more sensitive to laws leaving old grievances unaddressed. It is also worth noting that while the effect of domestic trials is magnified in Model 3, international trials and foreign trials also prove statistically significant. International trials are supportive of a more stable peace, but foreign trials create more risk of conflict recurrence. In Model 4, none of these effects are present. The lesson to be drawn from this comparison is that institutions of strong
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accountability and retributive justice, either domestic or international, are peace-promoting in those places where they are proceeding along with other democratic institutional developments. By contrast, truth commissions in cases of democratic transition are counter-productive, as are efforts from individual foreign states to attempt to impose justice from the outside. Democratizing peoples, it seems, favor firmer justice to airing of ‘truths,’ and they prefer that justice be provided by their own governments or organs of the United Nations. Finally, Model 3 also shows that even rebel victories preceding democratic peace spells lower the risk of future violence, as do ceasefire agreements. One might surmise that this indicates a greater satisfaction in nascent democracies with whichever group or method accomplished the feat of conflict termination. In the non-democracies represented by Model 4, however, only government victory is powerful enough to lower the risk of future outbreaks of violence. Finally, Model 5 repeats Model 2 for the full sample, except it substitutes the truth commission variable used in Models 1-4 with an alternate measure. The alternate measure, alluded to in footnote 12, does not sustain truth commission year coding beyond the spell in which a truth commission completed it operations. Unlike trials and amnesty laws, which have more continuous properties, truth commission operation is a discrete institutional event with a finite end. When we switch measures and re-run the model, all of the variables remain consistent with Model 2, with the exception of Polity squared and the new truth commission variable, which changes direction and loses significance. This makes us highly suspicious of our truth commission findings, but also of our regime type findings. Although we checked for correlations between these variables and others, finding none that were abnormally high, we remain unsure of the stability of the findings regarding truth commissions especially. Thus, we caution against grand theoretical inferences based on this particular set of results.
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Discussion and Conclusion Our findings suggest a more nuanced view of the peace versus justice debate and suggest several policy recommendations. First, most human rights trials are less risky than many assume. Contrary to other cross-national studies, we find domestic trials to be consistently associated with more durable periods of peace. They do not appear to exacerbate tensions or generate new grievances, at least not to the extent of leading to renewed violence that leads to 25 or more battle-related deaths in a given year. Given that the risk of conflict resumption falls with each additional year of domestic trials, it also suggests that populations become increasingly accustomed to trials as they continue rather than become increasingly restive. International(ized) tribunals are peace promoting when they follow democratic transitions; following nondemocratic transitions, conflict is no more likely if the international community establishes a tribunal. Foreign trials, by contrast, increase the risk of conflict resumption in democratizing countries. Second, truth commissions should be approached carefully. In particular, extended truth commissions should be avoided. The finding that truth commissions are uniformly associated with greater risk of conflict recurrence is surprising from the point of view of transitional justice advocates. However, they appear to be consistent with other research that connects truth commissions to lower levels of human rights protection (Olsen et al. 2010; Wiebelhaus-Brahm 2010). Given how we measure truth commissions, the results are consistent with Hayner’s (2010) policy prescription that truth commissions be implemented quickly and for relatively short periods of time after transitions. Long, drawn-out investigations often reflect insufficient resources and cooperation to complete the job. This may generate resentment among those who want justice done, while emboldening others to utilize violence to achieve their goals. If created,
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truth commissions should be granted sufficient financial and personnel resources to plan and conduct an investigation relatively quickly. Nonetheless, other measurement strategies may influence the results. Third, amnesty laws do not enhance the prospects of peace, as many suggest. Amnesty laws are associated with a greater risk of conflict resumption, particularly in the context of nondemocratic transitions. This suggests that amnesty laws that are enacted by non-democratic governments are less credible in their substance or implementation. Moreover, more frequent use of amnesty laws seems to send a message of weakness and encourages the resumption of conflict. Still, while repeatedly confirmed in the statistical results, the negative impact of amnesties is preliminary. The reason is that different types of amnesties—those that release political prisoners, those that target former combatants, or those that shield high-level officials from prosecution—need to be separated in the data. Future research might explore how differences in who is targeted by amnesty laws influence their lasting effects. Our findings suggest that the international community should be concerned with only certain types of transitional justice interventions. Perhaps due to their perceived legitimacy or the international community’s ability to coerce parties given UN troop presence in countries that have tribunals, international tribunals and hybrid courts do not jeopardize peace. In fact, they make peace more durable in democratizing societies. At the same time, our findings suggest that individual governments should be cautious in their use of universal jurisdiction. Particularly in democratizing countries, foreign trials place peace in greater jeopardy. As Meernik et al. (2010) correctly point out, there are one or more ways in which transitional justice measures might affect the duration of peace. First, transitional justice may lead to legal and institutional reforms that promote peace. These properties are most closely with
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truth commissions. Our finding that truth commissions are associated with increased risk of conflict resumption may be an indication of the poor implementation record of truth commission recommendations. Second, transitional justice may remove perpetrators of mass violence from positions of authority. Trials do this most directly; it appears that at least domestic and international trials may contribute to eliminating spoilers. By contrast, truth commissions and amnesties do not achieve this, at least not independently. Third, transitional justice may deter future acts of violence. Our results indicate that domestic trials have the strongest deterrent effect. Finally, transitional justice may help promote civil society organizations interested in promoting peaceful norms of conflict resolution. Nonetheless, while our findings are suggestive of the means through which transitional justice measures influence the durability of peace, quantitative studies are poorly suited to test the relative importance of these potential causal mechanisms. As such, there is a clear need for further qualitative research in this area. Lastly, our study suggests several other questions with respect to the durability of peace in post-conflict societies. First, civil war studies, including our own, consider only battle deaths. Nonetheless, many transitional societies struggle to contain crime. Some argue that there are significant continuities between civil war violence and post-conflict crime. Moreover, there are often popular demands for draconian responses to crime, which may spiral into renewed violence and human rights abuses (Call 2007; Wiebelhaus-Brahm 2010). Unfortunately, broadly comparative cross-national crime data does not exist. Second, our measures of transitional justice could miss some important qualitative characteristics. For example, there are significant differences between different truth commissions and domestic trials. The quality of justice produced by transitional justice mechanisms of the same type could vary considerably based on factors such as institutional structures, resources, and personnel to name a few. This has
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consequences for how satisfied victims, former fighters, and the public at large are with transitional justice. Finally, we have attempted to isolate the independent effects of different accountability mechanisms. However, increasingly, different forms of transitional justice are used in the same country, whether simultaneously or sequentially. It would be beneficial to explore how different combinations and interactions affect the durability of peace spells. A final word. It is the nature of academics and critical observers to stress counterintuitions, and to isolate the negative consequences of unreflective progressivist actions. The world is better for this kind of intellectual pushback. However, at times such criticisms become ossified, and their authors become incapable of updating. In an intriguing historiography, Madeiline Fullard and Nicky Rousseau (2008) demonstrate convincingly that historians’ criticisms of the South African TRC had formed and frozen at the onset of the organization’s operation. These criticisms became rote, routine statements and re-statements for public and media consumption, even as commissioners went to great lengths to address them. In short, the people of the TRC learned and adapted, but their detractors did not. We are afraid a similar process might be taking place around the initiation of human rights trials, whether domestic or international. While these institutions and their practitioners work hard to avoid pitfalls learned from the past, the same ‘threat to peace’ disparagement is continuously trod out, almost dutifully. We are not sure if all human rights trials promote justice, or whether reconciliation remains a quixotic aspiration, but based on the most nuanced data available on conflict patterns, we can say that holding trials does not seem to inspire resumption of civil war.
To the contrary, truth
commissions and amnesties do need to be closely monitored and re-examined for their conflictinspiring potential. Regardless of our findings, any claims that are at root empirical need thorough fleshing out—before that, they need humility.
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Kaplan-Meier survival estimates
200 300 analysis time dtrsel2 = 0
dtrsel2 = 1
Table. Variable Summary Statistics
Characteristics of Previous Conflict
Characteristics of Conflict Termination
Human Rights Accountability
Duration of Conflict Government Conflict Territorial Conflict Maximum Number of Conflicts Maximum Intensity Risk Set Government Victory Rebel Victory Ceasefire Agreement Cessation through Low Conflict Peace Agreement UN Peacekeeping Operation Cumulative Amnesty Laws Cumulative Truth Commission Years Cumulative Domestic Trial Years Cumulative International Trial Years Cumulative Foreign Trial years Polity 2 Polity 2 Squared Total Population logged GDP per capita (2000 $) logged
N 32723 32723 32723 32723 32723 26132 32723 32723 32723 32723 32723 32723 32078
Mean 24.602 0.526 0.191 0.868 0.631 1.391 0.218 0.058 0.064 0.125 0.085 0.037 2.165
St.Dev. 57.948 0.499 0.393 0.703 0.721 0.751 0.413 0.234 0.245 0.331 0.278 0.189 2.394
Min 0 0 0 0 0 1 0 0 0 0 0 0 0
Max 530 1 1 8 2 6 1 1 1 1 1 1 16
32723 32723 32723 32723 32459 32459 30724 29203
0.413 0.849 0.325 0.176 2.109 46.413 16.296 6.964
1.316 2.347 1.820 1.075 6.478 30.553 1.363 1.323
0 11 0 19 0 18 0 18 -10 10 0 100 12.9 20.82 4.13 10.55