A New Look at Weak State Conditions and Genocide Risk

3.1 “Rationalist” motives for killing civilians

Assume a threatened regime “produces” a certain amount of political or territorial control (designated by Q) by using two “inputs”: fighting rebels (R) and killing civilians (C). It is clear that the threatened regime can attempt to achieve control (Q) by directly contesting the rebels (R), but why might it intentionally kill civilians (C)? Scholars have pointed to several answers to this question, the most prominent being that during intrastate war or other internal crises, civilians can provide critical resources to rebels such as financing, information, personnel, and safe havens (Kalyvas 1999; Valentino 2004, ch.3; Valentino, Huth, and Balch-Lindsay 2004, 383–385). By attacking civilians, a threatened regime may perceive that it is undermining a key source of support for the rebels. A related motive for a regime to attack (or threaten to attack) civilians is to prevent them from defecting to the rebels and instead to support the regime. This tactic, of course, can backfire and drive civilians to support the rebels, but this possibility raises the risk that civilians will be attacked. This is especially true in areas where the regime is losing territorial control. The loss of territory means the loss of a critically valuable resource in that territory, namely, civilians. It is a “dual loss” because the civilians are lost to the regime and they come to be controlled by the enemy and thus leveraged against the regime. Like the retreating general who destroys oil wells and other assets to deny them to the enemy, so can a retreating regime contemplate the mass destruction of civilians. Another related motive to destroy civilians is to maximize resource extraction and/or create political or ideological homogeneity within geographic areas that are deemed strategically significant to the regime in its contest with actual or possible future rebels (Valentino 2004, ch. 3).

3.2 Optimal choice and demand conditions for killing civilians

Anderton (2014a) uses the following specific functional form model to simulate conditions under which a threatened regime would choose to kill civilians:

(1)C, Rmax Q = AC+(Rδδ)A>0, δ>1,S.t. I = PcC+PrR (1)

where A is a productivity parameter for killing civilians (C), δ is a productivity parameter for fighting rebels (R), I is the regime’s resources or income, and P_c and P_r are the respective costs or prices of killing civilians and contesting rebels. In their civil war study, Fearon and Laitin (2003) identify three variables that characterize weak states: (1) anocracy, (2) new state status, and (3) low income. In the model in (1), income is present in the form of parameter I. The other two weak state variables, anocracy and new state status, can be theoretically connected to the productivity parameter δ. States that are institutionally strong will be effective in contesting rebels, everything else the same, which will be reflected in a relatively high δ value. Institutionally weak states, however, will have a relatively low δ value.

Table 2 shows simulations of (1) for specific values for A, δ, I, P_c, and P_r. The table illustrates “optimal” choice or demand conditions for killing civilians. Rows 1–4 show that greater institutional weakness of the regime (lower δ), increases the quantity demanded for civilian killing (C*). Rows 3, 5, and 6 show that lower income (I) and output (Q) correlate to a greater quantity demanded for civilian killing. Hence, civilian killing is an inferior input for the parameter values in Table 2. Rows 3 and 7–9 show the “law of demand,” namely, that an decrease in the cost or price of killing civilians (P_c) leads to an increase in C*. Rows 3 and 10–12 show that a higher cost or price of contesting rebels leads to substitution into civilian killing such that C* rises. More generally, rows 3 and 7–12 imply that killing civilians and contesting rebels are gross substitutes for the parameter values shown because ∂C*∂Pr>0 and ∂R*∂Pc>0.

3.3 Hypotheses of genocide risk

The model in (1) and the results in Table 2 suggest empirically testable hypotheses of genocide risk. The starting point of the theoretical model is a regime’s perception of threat to its political or territorial control. Such losses can be perceived as highly deleterious to authorities because they may lose most or all of their privileges and face retribution (including incarceration or execution) following a loss of power. It is the perception of loss of control by an authority group that activates the constrained rational choice model in (1) (i.e., brings it into being) and, in so doing, brings the possibility of civilian killing into the authority group’s calculations. Hence, everything else the same, we hypothesize:

H1: The greater the threat against a state’s political authorities, the greater the risk of genocide onset.

As noted in rows 1–4 of Table 2, as the regime’s productivity parameter δ declines (i.e., it becomes weaker institutionally vis-à-vis rebels), it chooses more killing of civilians, everything else the same. According to Fearon and Laitin (2003), anocracies will be institutionally weak relative to autocracies and democracies. Hence, Table 2 suggests an inverted-U relationship between political system and killing civilians in which “intermediate political systems”, i.e., anocracies, will be at greater risk than autocracies and democracies, everything else the same:

H2: Anocracy relative to autocracy and democracy will increase the risk of genocide onset (inverted-U hypothesis).

New state status also suggests institutional weakness and a correspondingly high risk for civilian killings. For example, Fearon and Laitin (2003) maintain that new states tend to have untested military forces, which means that they would be relatively unproductive in contesting rebels should war come. Moreover, new states may be recognized as states by international organizations, but not necessarily by population groups in regions that were opposed to the current group before it came into power (Hironaka 2008, 75). Furthermore, according to Rotberg (2003, 19), new states often do not have a large number of experienced professionals and bureaucrats within the regime, thus making them vulnerable to external shocks and internal crises. Everything else the same, we hypothesize:

H3: New state status will increase the risk of genocide onset.

Table 2 also shows an inverse relationship between income/output and civilian killing in rows 3, 5, and 6. Hence, everything else the same, we hypothesize:

H4: Low income will increase the risk of genocide onset.

The purpose of our empirical inquiry is, conditional on threat, to focus upon weak state conditions and genocide risk, but we also want to consider other independent variables noted in Table 1. Another important variable to consider when assessing genocide risk is discrimination. Genocide scholars have shown how people from an in-group can come to disassociate with and dehumanize people from an out-group through severe discrimination (Fein 1977, 1979, 1993; Waller 2007). Such “othering” of an out-group can have a variety of possible impacts on the authority group’s rational choice calculations modeled in (1). For example, an aggrieved group might be prone to start a rebellion against the state or join a rebellion already under way. This could raise the cost or price to the state of contesting rebels, which could lead to more civilian killing, everything else the same, which was shown in rows 3 and 10–12 of Table 2. Furthermore, discrimination could affect an authority group’s price of killing civilians. If a potentially targeted civilian group faces substantial discrimination, it would be relatively easy for the authorities to recruit perpetrators against the out-group, everything else the same. The inverse relationship between the cost of killing civilians and the “optimal” amount of civilian killing is demonstrated in rows 3 and 7–9 of Table 2. We hypothesize:

H5: Greater discrimination will increase the risk of genocide onset.

The cost or price of killing civilians may have been relatively low during the Cold War owing to the superpower stalemate. In the post-Cold War period, the price of killing civilians may be higher, everything else the same. For example, new anti-atrocity institutions emerged in the post-Cold War period (e.g., International Criminal Court, R2P) and about 75% of all UN peace missions began after 1989, which encompasses only about only 33% of the years in which the UN has existed (Anderton 2014a). We hypothesize:

H6: The Cold War period will correlate to a greater risk of genocide onset.

Two other variables in Table 1, trade and ethnic fractionalization/polarization, have received mixed results in empirical studies of civilian atrocities. Hence, we consider them in our extended analysis in Section 6. Because countries in the international system vary widely in size, we include population as a control variable in all our regressions. We make no hypothesis about the relationship between genocide onset and population but note that population has been a control variable in other mass atrocity empirical studies (e.g., Aydin and Gates 2008; Colaresi and Carey 2008; Easterly, Gatti, and Kurlat 2006; Kim 2010; Krain 2012, 2014; Valentino, Huth, and Balch-Lindsay 2004).^[8]

4.1 Model and variables

Guided by the discussion in the previous section, we specify our initial empirical model as:

(2)Prob(Onset=1)=Λ(β1+β2Population+β3Threat+β4Monopoly_Control++β5Monopoly_Control_Squared+β6New_State+β7Income+β8Discrimination+β9Cold_War), (2)

where Λ is the logistic cumulative distribution function defined on country-year observations.^[9] As has been learned in the more fully developed civil war literature, occurrence as the dependent variable conflates issues of onset and termination. We adopt the country-year as our unit of analysis, rather than regimes and/or longer time intervals, which also mirrors successful practice in civil war research. And we use 1955–2006 for our time frame, which carries us as close to the present as our data sources permit. Here we indicate the measures for the variables in (2), highlighting alternative measures later as needed. Table 3 presents descriptive statistics.

Onset: Our dependent variable is the probability of genocide onset, where Onset equals one in the initial year of a genocide and zero otherwise. We adopt the list of 41 genocides and politicides compiled by the Political Instability Task Force (PITF) in its State Failure Problem Set 1955–2010 (Marshall, Gurr, and Harff 2010). PITF takes care to distinguish analytically between civil wars and genocides, where the latter are characterized by “authorities’ systematic targeting of noncombatants” (Marshall, Gurr, and Harff 2010, 15). Since PITF includes both genocides and politicides in the same dataset and within the same definition (as shown in footnote 5), we make no distinction between genocides and politicides in our coding. This practice has been followed by others in the empirical literature who have used either Harff’s (2003) list of genocides and politicides or the PITF geno-politicide dataset (e.g., Aydin and Gates 2008; Besançon 2005; Colaresi and Carey 2008; Goldsmith et al. 2013; Kathman and Wood 2011; Krain 2005, 2012, 2014; Rost 2013). From this point forward we use the term “genocide” to encompass both genocides and politicides.

Population: Because countries in the international system vary widely in size, we include a measure of population as a simple control variable. Our measure Population is drawn from the Penn World Table (PWT) Version 7.1 (Heston, Summers, and Aten 2012) and is defined as the natural logarithm of population scaled in millions.

Threat: For a measure of threat, we turn again to PITF’s State Failure Problem Set 1955–2010, which gauges the magnitude of revolutionary and ethnic wars on a country-year basis. This source is suitable for several reasons. First, as noted above, PITF is deliberate in its analytical distinction between civil war and genocide. Second, PITF applies lower and hence more inclusive selection thresholds, meaning that PITF identifies more intrastate conflicts than do other prominent sources. And third, PITF estimates the magnitude of conflict over a larger range (five-point scale) relative to other major conflict data sources. This latter point is relevant when considering, not just the presence, but also the magnitude of potential threat against government authorities. As our results later will reveal, our measure of threat remains significant, even after controlling for the presence of war.

For each year of a revolutionary or ethnic war, PITF codes a five-point scale called Magarea based on estimates of the “portion of [a] country affected by fighting.” The scale takes on values of 0 (less than one-tenth of the country and no significant cities directly or indirectly affected), 1 (one-tenth of the country and/or one or several provincial cities directly or indirectly affected), 2 (more than one-tenth and up to one quarter of the country and/or the capital city directly or indirectly affected), 3 (from one-quarter to one-half the country and/or most major urban areas directly or indirectly affected), and 4 (more than one-half the country directly or indirectly affected). From these data we construct our measure Threat. In cases of no war, we impute the value of zero; in cases of either revolutionary or ethnic war alone, we set Threat equal to the Magarea value; where both war types occur simultaneously, we set the measure equal to the maximum of the two Magarea values. For robustness, we also consider PITF’s equivalently-constructed Magfight measure, which gauges the magnitude of combatants or activists opposing the state. By H1, we expect Threat to have a positive effect on the probability of genocide onset.

Monopoly control and monopoly control squared: Our measure of political control ultimately draws from the Polity IV Project: Political Regime Characteristics and Transitions, 1800–2010 (Marshall, Gurr, and Jaggers 2010). We begin with the widely used composite measure Polity2, which is a 21-point scale that ranges from –10 for full autocracy to +10 for full democracy. Polity2 is described in the user manual as a combined score revised such that cases of foreign interruption (with standardized authority score –66) are treated as missing, cases of interregnum or anarchy (–77) are set to zero, and cases of transition (–88) are interpolated when feasible. We make three modifications to the Polity score. First, we incorporate additional Polity2 observations available in Gleditsch (2008), where some missing scores are estimated, extrapolated, or drawn from an earlier version of Polity. Second, we modify the Polity2 protocol by treating cases of interregnum or anarchy (–77) as missing rather than imputing a neutral score of zero. Third, to facilitate interpretation as a measure of monopoly control, we simply translate the Polity2 score so that it ranges from 0 for full democracy to 20 for full autocracy.

In an important critique, Vreeland (2008) shows that use of Polity data can be problematic because two of its five underlying components are sensitive to observed civil war or genocide. Specifically, Polity2 data contain an aggregation of five component scores pertaining to executive power (XCONST, XRCOMP, and XROPEN) and political participation (PARREG and PARCOMP) as shown in the Polity codebook (Marshall, Gurr, and Jaggers 2010). Vreeland shows that civil war or genocide enters the coding of the two participation components. For PARREG, for example, Vreeland quotes from an earlier codebook that under the category of factional/restricted are “polities in which political groups are factional but policies of genocide or politicide are routinely carried out against significant portions of the population” (Gurr 1990, 17). Moreover, such instances of political violence are assigned a coded numerical value toward the middle of the range of PARREG and PARCOMP, possibly generating a spurious inverted-U relationship between Polity and political violence. Vreeland shows that this can be avoided by constructing an alternative index based only on the three executive components.

Following Vreeland, we construct an alternate measure by summing the remaining three uncontaminated Polity2 components and then applying the same protocols previously described for the Polity2 data. The resulting measure, labeled Monopoly Control, gauges monopoly power of the executive and ranges from 0 for perfect democracy to 13 for perfect autocracy. Our reconstructed Polity measure removes the contaminated elements and it focuses the measure on the executive decision-makers within the state because the three remaining components have to do with executive power. By H2, we expect Monopoly Control to display an inverted-U relationship in which anocracy shows a higher risk of genocide than autocracy and democracy.

We believe that our use of adjusted Polity data is important because use of contaminated Polity is widespread in the empirical civilian atrocities literature. Of the 22 empirical studies listed in Table 1 which include one or more measures of political regime, 20 use unadjusted Polity scores.^[10] Moreover, to the best of our knowledge none of the empirical studies in the civilian atrocity literature test for an inverted-U relationship between political regime and civilian atrocities using uncontaminated Polity data. Aydin and Gates (2008) identify the contamination issue and adjust for it by using uncontaminated components of Polity and Vanhanen’s data on electoral participation, but they do not test for an inverted-U relationship between political regime and civilian atrocity risk.

New State: As we will show, our sample is an unbalanced panel of nations, many of which enter as new states. To allow for this entry, we define New State as a dummy variable equal to one if a country’s age is 5 years or less and equal to zero otherwise. To the best of our knowledge, Rost (2013) is the only published article in the empirical genocide literature that directly tests for the effects of new states but he does not report his methods or empirical results. Rost indicates in an appendix that the absence of new states correlated to a greater genocide risk. By H3, however, we expect New State to have a positive effect on genocide onset.

Income: Our measure labeled Income is drawn directly from the PWT 7.1 and is the natural logarithm of real GDP per capita in thousands of chained 2005 international dollars. By H4, we expect Income to have a negative effect on genocide onset.^[11]

Discrimination: We derive our measure of discrimination from the Minorities at Risk (MAR) Dataset (Minorities at Risk Project 2009). MAR tracks through 2006 the annual experience of close to three hundred communal groups in countries with populations of at least 500,000. For a given country-year, MAR determines five-point indexes of political and economic discrimination for each qualifying group. Political discrimination pertains to “exercise of political rights or access to political positions,” while economic discrimination refers to “access to desirable economic goods, conditions, or positions” (Gurr 2000, 109, 111). The values of the political index are 0 (no discrimination), 1 (under-representation due to historical neglect or restrictions but with remedial policies), 2 (under-representation due to historical neglect or restrictions but without remedial policies), 3 (under-representation due to dominant social practices but with neutral policies), and 4 (formal policies of exclusion and repression). The economic index is defined in a commensurate manner. For our purposes, it is worth noting that the index value of 4 “does not include repression during group rebellions” but “does include patterned repression when the group is not openly resisting state authority” (Codebook, 11).

From these data we define the measure Discrimination as follows. For a given country-year, if MAR shows no communal group at risk, then our measure is imputed the value zero; otherwise, it is assigned the highest level of political or economic discrimination determined by MAR for any qualifying group. Notice that we make no attempt to match a particular group in MAR with the victim group in a genocide case. Hence Discrimination measures the highest level of discrimination evidenced in a country against any group. We prefer this approach to measuring discrimination because we seek to capture the general discriminatory (“othering”) capacity of the state regardless whether groups facing discrimination become victims of genocide. By H5, we expect Discrimination to have a positive effect on genocide onset.^[12]

Cold War: To allow for a systemic change in international relations, we define Cold War as a dummy variable equal to one for all years through 1989 and zero thereafter. By H6 we expect Cold War to have a positive impact on genocide onset.^[13]

4.2 Sample and estimation

Sample construction begins with 178 independent states identified by Gleditsch and Ward (1999). The initial temporal range is 1955 through 2009 based on the coverage in the PITF list of genocides. To avoid conflating issues of onset and duration, we drop from the sample all country-years that involve ongoing genocides. The sample is further reduced by missing observations associated with particular measures included in the regressions. The resulting basic sample consists of 5913 observations involving 155 countries spanning the years 1955 through 2006. Included are 32 genocide onsets occurring in 24 countries.^[14] We structure the sample as an unbalanced panel and then estimate the model using logit regression. To reduce simultaneity issues, all right-hand variables except New State and Cold War are lagged 1 year.

5.1 Basic model

The estimated coefficients and cluster-robust standard errors for our basic model are reported in column (1) of Table 4. For convenience we show two-sided p-values, noting however that most of our hypothesis tests are properly one-sided. Consistent with our expectations, the measures for Threat, New State, Discrimination, and Cold War, all have statistically significant positive effects. Coefficient estimates for Monopoly Control and Monopoly Control Squared are also statistically significant and consistent with an inverted-U relationship between political regime and genocide onset. Income has its expected negative effect and is significant. The coefficient on Population has a positive sign (with no prediction) and is significant.

5.2 Monopoly control and inverted-U

As noted earlier, Vreeland’s (2008) critique of the Polity contamination issue indicates that instances of political violence are assigned numerical values toward the middle of the Polity components PARREG and PARCOMP. Hence, unadjusted Polity data might identify a spurious inverted-U relationship between Polity and political violence in which anocracies appear to have a greater risk of conflict than democracies and autocracies, everything else the same. This is indeed what Vreeland found after adjusting the Polity data for two prominent civil war studies (i.e., Fearon and Laitin 2003; Hegre et al. 2001). To the best of our knowledge seven published studies test for an inverted-U relationship between Polity and civilian atrocities, with DeMeritt (2012), Hultman (2012), Goldsmith et al. (2013), and Rost (2013) finding evidence in favor of the relationship, but these studies use unadjusted Polity data.^[15] Aydin and Gates (2008), however, adjust for the contamination issue, but they do not test the inverted-U hypothesis.

To the best of our knowledge, column (1) of Table 4 represents the first reported test in the empirical genocide literature of the inverted-U hypothesis using adjusted Polity data. Whereas Vreeland found that the inverted-U result vanished in his tests of civil war risk, we find significant evidence for an inverted-U relationship between adjusted Polity and genocide risk. We re-ran the same model using unadjusted Polity data and results are reported in column (2) of Table 4. Coefficient estimates for Monopoly Control and Monopoly Control Squared cannot be directly compared across the columns of Table 4 because adjusted Polity data are based on a 0–13 scale while unadjusted Polity follows a 0–20 scale. Nevertheless, column (2) also reports significant evidence for an inverted-U relationship. Hence, the risk of genocide onset is higher for anocracy relative to autocracy and democracy for both adjusted and unadjusted data. Although our coefficient estimates are not substantially different when we switch from adjusted to unadjusted Polity data, future research should use adjusted data. Consider first that the risk of genocide associated with intermediate Polity scores is greater for unadjusted relative to adjusted data.^[16] Moreover, in column (2) the positive coefficient estimate on New State ceases to be significant (albeit barely). Hence, use of unadjusted Polity may over-estimate genocide risk for anocratic levels of Polity and potentially affect the statistical significance of other variables.

6.1 Trade openness

As noted in Table 1, numerous empirical studies consider the effect of trade openness on civilian atrocity risk or seriousness. For a country’s trade openness, we again draw from the PWT 7.1, defining Openness as exports plus imports as a percentage of real GDP. If genocide interrupts international trade flows and relationships, thereby making violence more costly, then genocide would be less likely for more economically integrated states, everything else the same. In Table 5 we repeat the basic model results in column (1) and then show in column (2) what happens when we enter our measure for openness. Note that the coefficient on Openness has a negative sign as predicted but is near zero and far from significant.^[17]

6.2 Ethnic heterogeneity

Here we explore the familiar proposition that the risk of genocide is higher in ethnically diverse countries, where divisions are facilitated along group lines (Chalk and Jonassohn 1990; Fein 1977). Citing Horowitz (1985), Montalvo and Reynal-Querol (2008) emphasize the related proposition that genocide is more likely when a country is polarized, meaning that a large majority is set against a large minority. In their logit model of genocide occurrence, Montalvo and Reynal-Querol find no statistical effect for fractionalization but a strong positive effect for polarization.^[18] To test these propositions we compute measures of fractionalization and polarization based on country-specific, time-invariant ethnic group shares provided in Alesina et al. (2003). As shown in column (3) of Table 5, we find no statistically significant evidence that greater ethnic heterogeneity increases the risk of genocide.

6.3 War

In column (4) of Table 5, we include a dummy variable for internal war (ethnic or revolutionary) based on the PITF intrastate conflict dataset. Note that the coefficient estimate on Threat remains positive and significant, while the coefficient for War has the correct sign but is far from significant. In results available from the corresponding author, we find that when we substitute the War dummy for our measure of Threat, we obtain the correct sign and statistical significance for the War coefficient. However, that model has lower pseudo R-square and log likelihood relative to the basic model. Hence, we find that our more graduated index of Threat outperforms the war measure. We also ran the basic model with a Magfight measure of Threat that is constructed in a similar fashion to the Magarea index. Magfight performs essentially equally well to the Magarea measure (results available from corresponding author). Many others have controlled for the presence of war in their empirical studies of civilian atrocities.^[19] We find that PITF’s Magarea and Magfight indexes generally outperform these war measures.

6.4 Real growth

Per capita income has been interpreted in multiple ways in empirical studies on conflict. For example, some interpret it as a proxy for the opportunity cost of forgone employment in the regular economy should one participate in the activities of a violence-producing organization (e.g., Collier and Hoeffler 2004). Others treat per capita income as one of the measures of a weak state (e.g., Fearon and Laitin 2003). Our objective is not to settle what might be the most appropriate interpretations of per capita income. Indeed, how it should be interpreted likely varies across conflict types and authors’ samples. Nevertheless, we attempt to narrow the range of interpretation by controlling for the growth rate of real gross domestic product. Our measure, called Real Growth, is taken from Penn World Table (PWT) Version 8.0 (Feenstra, Inklaar, and Timmer 2013) and entered with a 1-year lag. We hypothesize that lagged real growth would capture economic conditions, and thus employment opportunities, in the regular economy. Hence, real growth would capture in part the opportunity cost of forgone employment, leading to an inverse relationship between real growth and genocide risk. Results reported in column (5) of Table 5 show that real growth has the predicted sign but is insignificant. Moreover, the coefficient estimate on per capita income remains negative and significant. We take these results as not ruling out the weak state interpretation of per capita income and the possibility that killing civilians has inferior input characteristics.^[20]

6.5 Political and economic discrimination

Recall that our measure of discrimination relies on two underlying measures – one being the highest level of political discrimination evidenced against any communal group within a country-year, and the other being the same for economic discrimination. Because the MAR measures are defined commensurately, we can examine whether the two forms of discrimination have similar effects on genocide. In Table 5 we show in column (6) what happens when we enter both measures of discrimination. Note that the effect of political discrimination is close to zero and insignificant, while the coefficient on economic discrimination is positive and significant. The two measures are highly correlated (r=0.808), which likely accounts for why the hypothesis of equal effects cannot quite be rejected at conventional significance levels (χ²(1)=1.34, p=0.247). It is evident, however, that the explanatory power is carried primarily by economic discrimination. In results available from the corresponding author, if economic discrimination is dropped, the log likelihood decreases markedly (from –155.101 to –159.461) and the pseudo R-square falls (from 0.220 to 0.198); yet if political discrimination is dropped, the two statistics hold stable (at –155.132 and 0.220).

Gurr and Moore (1997) found that economic as opposed to political discrimination significantly heightens the articulated grievances of minorities, but they provided no explanation for this finding. In our context pertaining to genocide risk, we have emphasized that discrimination can foster the “othering” of an out-group, which reduces the costs to an authority group of recruiting perpetrators. But economic discrimination can further reduce the costs of recruitment by rendering acceptable the seizure of victims’ wealth. Moreover, undercutting a victim group’s economic livelihood may be particularly damaging to the group’s viability and thus an important precursor to genocide (people can live without voting rights, but not bread). Thus, economic discrimination can especially elevate the risk of genocide.

6.6 Cold war and the internet

In our basic model in column (1) of Table 5, the positive and significant coefficient on the Cold War indicator is consistent with the hypothesis that tensions between the major powers prior to 1990 made cooperative intervention less likely and hence increased the risk of genocide. However, it is also intriguing to consider that the post-Cold War period roughly coincides with the emergence of new information technologies (e.g., satellite television, the globalization of CNN, the internet, mobile phones, social networking, etc.) that facilitate awareness of mass atrocities. Hence, leaders contemplating genocide might consider the greater awareness and risk of intervention that now exists relative to the Cold War period. One conjecture is that if this spread of information facilitated third-party reaction, the rapid advance of internet technology after 1989 could have lowered the risk of genocide and hence generated a positive coefficient on the Cold War dummy. Of course, governments can use information technologies to suppress citizens, including perpetrating civilian atrocities, so our conjecture is speculative. The important point is that, to the best of our knowledge, large-sample empirical civilian atrocity studies published to date have not assessed the possible impact of information technology. We check for this possibility by adding to our basic model a lagged measure of the number of internet users per 100 persons in a given country-year (World Bank 2011).

As shown in column (7) of Table 5, Internet Users per 100 has a negative effect as conjectured but is not statistically significant, with a one-sided p-value of about 0.17. Also, before leaving column (7), note that when Internet Users per 100 is added, the coefficient on Cold War increases from 1.352 to 1.460 and remains significant. Thus, controlling for internet technology, we still find evidence that genocide risk fell after the Cold War, other things equal.^[21]

6.7 Other estimation issues

When applying logit to time-series cross-section data, temporal dependence can arise (Beck, Katz, and Tucker 1998), which in this context exists if the likelihood of genocide onset depends on a country’s chronological experience regarding genocide. Among methods for modeling dependence, the application of a cubic polynomial is appealing for its simplicity and demonstrated performance. Following Carter and Signorino (2010), we add to our basic model a polynomial consisting of the number of prior genocide-free years and that same number squared and cubed. In column (8) of Table 5 we show that all three polynomial terms are statistically insignificant, and the joint hypothesis of zero coefficients cannot be rejected (χ²(3)=0.800, p=0.849). The coefficients on the other variables in the model are qualitatively unaffected.

For random effects, reported in column (9), the coefficient estimates are similar, and a Breusch-Pagan test that the within-country serial correlation ρ equals zero cannot be rejected at conventional significance levels (χ²(1)=0.002, p=0.483).^[22] Regarding fixed effects estimation, the method is severely stressed when the event of interest is rare (Beck and Katz 2001). This means that countries experiencing no genocide onset are effectively dropped because their observations contribute nothing to the likelihood calculation. More appropriate to our study is rare events logit, which corrects for possible underestimation of rare event probabilities in finite samples (King and Zeng 2001a,b; Tomz, King, and Zeng 1999). As shown in column (10), estimation by rare events logit leaves the coefficients and their significance qualitatively unaffected.^[23]