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Angry or Weary?
How violence impacts attitudes towards peace among Darfurian refugees
Chad Hazlett
Abstract
Does exposure to violence motivate individuals to support further violence, or to seek
peace? Such questions are central to our understanding of how conflicts evolve, terminate,
and recur. Yet, convincing empirical evidence as to which response dominates—even in
a specific case—has been elusive, owing to the inability to rule out confounding biases.
This paper employs a natural experiment based on the indiscriminacy of violence within
villages in Darfur to examine how refugees’ experiences of violence affect their attitudes
toward peace. The results are consistent with a pro-peace or “weary” response: individuals
directly harmed by violence were more likely to report that peace is possible, and less likely
to demand execution of their enemies. This provides micro-level evidence supporting earlier
country-level work on “war-weariness,” and extends the growing literature on the effects
of violence on individuals by including attitudes toward peace as an important outcome.
These findings suggest that victims harmed by violence during war can play a positive role
in settlement and reconciliation processes.
Departments of Statistics and Political Science, 3264 Bunche Hall, Los Angeles, CA 90095. chazlett@ucla.edu. I thank
Jonathan Loeb, Ethan Siller, Benjamin Naimark-Rowse, and the entire 24 Hours for Darfur research team for their tireless
work, in addition to the U.S. Department of State for supporting that work. Thanks to Ron Rogowski, Graeme Blair, Jens
Hainmueller, Adam Berinsky, Fotini Christia, Daniel Posner, Dan de Kadt, Teppei Yamamoto, Daniel Hidalgo, Nicholas
Miller, members of the Boston Working Group in African Political Economy, and members of the UCLA Improving
Design in Social Science workshop for valuable feedback and discussion. Thanks also to Maryam Aljafan and Valerie
Wirtschafter for excellent research assistance.
1 Introduction
Large-scale violence directed against civilian populations is a common feature of many civil wars
(Valentino et al. 2004). Beyond the immediate and horrific human consequences of such violence, it
may also have long-term effects on diverse outcomes including political engagement (e.g. Blattman
2009), psychological well-being (see e.g. Pham et al. (2004)), education and employment (Blattman
and Annan 2010), and social cooperation (see Bauer et al. 2016 for review). An important—yet rarely
studied—question regarding violence is its effects on individuals’ support for further violence, on the
one hand, or for peace and reconciliation on the other. Popular accounts often hold that “violence
begets violence.” Yet, experiences with violence may instead heighten the desire to make peace or
reluctance to support continued fighting. Existing theories and evidence from a range of disciplines
make both claims. However, prior efforts to empirically determine how exposure to violence changes
individual attitudes toward peace have been stymied by confounding problems: Violence does not
occur at random, with those experiencing violence likely to differ in many ways from those who do
not. For example, the more bellicose, anti-peace individuals may take actions that increase their risk
of exposure to violence. Such confounding is difficult to rule out in many studies, and may bias naive
comparisons particularly towards showing that exposure to violence is associated with “angry” or “anti-
peace” attitudes. Solving the confounding problem requires more than controlling for an assortment
of observed covariates, which still leaves estimates vulnerable to unobserved confounding.
This paper employs a quasi-experimental strategy to estimate the effects of being injured or maimed
during attacks on villages in Darfur on attitudes. I argue that violence was targeted by village and
gender, but was indiscriminate beyond this. Comparisons within village and gender show that those
who were physically injured are 12-14 percentage points more likely to claim it is possible to make peace
with former enemies, and less likely to call for executing their enemies. This evidence is consistent not
with the “angry” response, but rather with claims of a “pro-peace” or “weary” effect of exposure to
violence. I discuss potential limitations, and in particular examine how strong remaining confounding
would need to be to alter the conclusions.
2 Background
Ample theoretical and observational support can be marshaled for either the proposition that “violence
begets violence,” or that “violence heightens war-weariness.” Here, I briefly describe literature related
to each proposition as well as closely aligned empirical research on how exposure to violence affects a
1
range of other outcomes.
2.1 Violence begets violence
Arguments from numerous disciplines, not to mention journalistic accounts and folk theory, hold that
exposure to violence during conflict makes civilians more likely to support calls for further violence or at
least resist appeals for peace. A parsimonious explanation for why violence should beget violence can be
gleaned from the security dilemma (Posen 1993): Groups who have fought in the past cannot trust each
other to keep peace in the future, and may choose to preventively attack the other group in the name
of their own security. In this framework, exposure to violence need only have an informational effect:
it reveals that neighbors have the capacity and the willingness to attack – and thus may do so again.
For example, Hayes and McAllister (2001) find in Northern Ireland that community experiences with
violence are followed by reduced support for decommissioning paramilitary weapons out of heightened
concern for their own security.
Fear or hatred, psychological trauma, or cultural motives such as demands for retribution are
not required for the security dilemma to operate, but have been called upon in political science,
medicine, and social psychology as explanations for why violence should beget violence. Individuals
from victimized communities may experience emotions of fear, hatred, and resentment, driving them to
take up arms or to otherwise support further violence against their perpetrators (e.g. Petersen 2002).
These emotional reactions may be transmittable across generations (see e.g. Balcells 2012; Rozenas
et al. 2017; Zhukov and Talibova 2018; Osorio et al. 2018). A psychiatric literature considers the
consequences of violence through post-traumatic stress disorder (PTSD) and depression (Pham et al.
2004; Vinck et al. 2007; Pham et al. 2009), suggesting that PTSD is associated with less openness to
reconciliation and greater desire vengeance (Bayer et al. 2007), or with identifying violence as a means
to achieve peace (Vinck et al. 2007). Exposure to terrorist violence may heighten psychological distress
and threat perception, “foment[ing] political attitudes eschewing compromise and favoring militarism”
(Canetti et al. 2013), or leading to “greater militancy over time” (Hirsch-Hoefler et al. 2016).1
Finally, social and cultural expectations that individuals seek retribution can support a the violence-
begets-violence claim. One influential account is the “culture of honor” (Nisbett and Cohen 1996),
which proposes that communities unable to rely on outside protection must develop reputations for
1However, several other studies find that pro-peace (“weary”) or more militant (“angry”) responses are both possible
depending upon other factors. In Colombia’s 2014 election, Weintraub et al. (2015) finds “an inverted-U relationship”
between exposure to violence by insurgents and support for the pro-peace candidate.Huddy et al. (2005) finds that
individuals who responded to the 9/11 terror attack with anxiety appear to be more pro-peace, while those who respond
with heightened threat perception appear to be more bellicose.
2
toughness. When attacked by outsiders, such groups must seek vengeance as a means of deterring
future attacks. Members of attacked communities are rewarded for seeking revenge, and sanctioned for
failing to do so. This may be an apt description of norms observed among Darfurian refugees (Hastrup
2013).
2.2 Violence begets weariness
However deeply entrenched the violence-begets-violence view may be in popular and academic accounts,
there are also many competing claims. First, the shorthand of “weariness” used here is borrowed from
a long-standing body of work on “war weariness” in international relations (see Levy and Morgan
1986. While posited at the level of inter-state behavior, these theories have nevertheless often projected
micro-level responses to violence onto state behavior. For example, Toynbee (1954) proposed a learned-
consequences argument for war-weariness, arguing “the survivors of a generation that has been of
military age during a bout of war will by shy, for the rest of their lives, of bringing a repetition of this
tragic experience either upon themselves or upon their children.” The present study offers micro-level
evidence in support of these long-standing war-weariness accounts.
One simple logic for the pro-peace response to violence is that of differentially-revealed costs, or
learned consequences. Individuals who face the most severe and salient costs of violence by more
directly or intensely experiencing it may more often conclude that it is too costly, making peace a
more palatable option. Tellez (2018) employes such an argument to explain why Colombian civilians
living in areas with higher FARC violence show greater support for peace with the FARC, according
to both survey data and results of the 2016 referendum. Similar arguments have been made by Bakke
et al. (2009) to explain why, in a survey of 2000 individuals surveyed in the North Caucasus, those
“relatively close to violence are more willing to engage in post-conflict reconciliation.” In a survey
experiment in Pakistan, Fair et al. (2016) find that those primed to perceive the country as more
violent were less supportive of militant organizations, arguing that “[a]s civilians experience increased
costs of militant violence, they may be less likely to see militant groups as a solution to their grievances;
instead they may come to see militants as a source of threat and disruption.”
Psychological arguments have also been made in support of a “weary” response. While PTSD due to
violence has been linked to more bellicose attitudes, those who respond to violence with depression may
show the opposite, more “weary” response (Vinck et al. 2007). Now ubiquitious in several literatures
and journalistic accounts are appeals to “post-traumatic growth” theory (Tedeschi et al. 1998; Tedeschi
and Calhoun 2004), which proposes that experiences of trauma can lead survivors to become more
3
altruistic and socially engaged. This has been invoked to explain recent quasi-experimental findings
that exposure to violence leads to increased social engagement (Bellows and Miguel 2009; Blattman
2009) and increased altruism (Gilligan et al. 2011; Voors et al. 2011). Returning to the FARC example,
Krause (2017) explains a similar finding to that of Tellez (2018) by arguing that violence leads to post-
traumatic growth resulting in greater empathy.
Finally, this study can be placed in an emerging body of literature employing (conditionally)
random variation in exposure to violence to more confidently rule out confounding concerns. Beber
et al. (2012) examine local randomness in exposure to violence during riots in Khartoum, Sudan,
finding that exposure to violence appears to increase support for allowing South Sudan to secede.
These results may at first suggest a “weary” reaction, since secession may bring about peace, even at
the presumed cost of weakening Sudan’s economy and granting those who caused violence precisely
“what they wanted.” However, secession would also exile members of the opposing group (southerners),
and such a partition hardly suggests a desire for peacemaking. Hence, the implications of this finding in
terms of attitudes toward peace as studied here remain unclear. More broadly, recent years have seen a
growing number of studies—many employing arguably random variation in exposure to violence—that
find “pro-social” effects of exposure to violence on cooperation and civic engagement, as reviewed in
Bauer et al. (2016). Such “pro-social” effects do not have clear implications for the “angry” or “weary”
question: As Bauer et al. (2016) remark, “the rising social cohesion we document need not promote
broader peace.”2Hence, while some effects of violence studied thus far are arguably pro-social, the
consequences of these effect for attitudes toward peace with out-groups remain ambiguous.
2.3 Violence in Darfur
This study examines attitudes among refugees from Sudan’s western states, known collectively as
Darfur. While Darfur has experienced previous wars and sporadic violence, the conflict studied here
erupted in February 2003, when two rebel groups—the Sudan Liberation Army (SLA) and the Justice
and Equality Movement (JEM)—launched an attack on the government air force base in Al Fashir,
the capital of North Darfur state. The motives articulated for this rebellion by the armed movements
included long-standing neglect of the region by the central government and a history of attacks on
civilians by both the Sudanese army and irregular militia widely referred to as the Janjaweed (Flint
2In addition, many of these studies examine only within-group behavior, not attitudes towards a participant has toward
an out-group member, much less one who has perpetrated horrific violence against them and their community. Some
evidence suggests that the apparent increase in social cohesion is principally parochial in nature (e.g. Rohner et al. 2013;
Choi 2007). By contrast, Hartman and Morse (2017) investigate the effects of violence on attitudes towards members of
other groups, and find increased empathy, a result they too link to post-traumatic growth.
4
and de Waal 2008). In response to the early success of this rebellion, the government unleashed a
ferocious counter-insurgency operation designed to punish, kill, or displace the civilian population of
ethnic groups presumed to be broadly supporting the uprising. Violence rates climbed and remained
high through 2003 and 2004 (Flint and de Waal 2008), directed against entire civilian communities.
Most refugees or internally displaced persons left their homes during 2003-2004. A large number
of those in the western regions of West Darfur made the decision to cross the border into eastern
Chad. Very few of these refugees had returned home by the time of this survey in mid-2009, when
approximately 250,000 Darfurians were registered in refugee camps in eastern Chad.
The number of people killed during the height of violence remains unclear. Estimates suggest that
in the 17 months from September 2003 to January 2005, there were 120,000 excess deaths attributable
to the conflict, of which 35,000 were due to direct violence (Guha-Sapir and Degomme 2005). Over
the wider course of the conflict, Degomme and Guha-Sapir (2010) find that for the period of 2004-
2008 approximately 300,000 deaths were attributable to the conflict, amounting to roughly 5% of the
pre-2004 population.
It is important to note that the logic of violence in Darfur in 2003-2004 was not rooted in a contest
for civilian support (as in Kalyvas, 2006). It was instead designed to “drain the sea” (Valentino 2005),
attempting to kill or drive out whole communities thought to support the armed movements. Because
villages in this area were extremely homogeneous ethnically (and by presumption, politically), the
government and militias’ efforts to target particular groups (including the Fur, Zaghawa, and Masalit)
was tantamount to targeting their villages. However, as detailed at length in Section 3.3, within
these villages and for people of a given gender, violence was arguably untargeted or“conditionally
indiscriminate”.3
3 Methods
The analysis is designed to maximize the credibility with which an observed association can be regarded
as causal, while being transparent as to its limitations. After describing the main variables and
measurement decisions, I describe qualitative evidence for the central identifying assumption that
3Because the term “indiscriminate” does not specify the level at which it is indiscriminate versus targeted, I prefer
the term “‘conditionally indiscriminate”. This directly conveys that statistical properties required for the identification
strategy: Conditional on something (village and gender), violence is distributed without reference to additional charac-
teristics consequential to the outcome, and can be treated as random within members of that particular stratum. This
in no way implies that violence can be treated as random or indiscriminate across those strata—i.e. some villages may
experience more violence than others. Straus’s terminology of “group selective” (Straus 2015) is also appropriate here,
to designate that at some level, violence is purposefully targeted (here, towards groups based on village and gender here)
while it is possible for violence to be experienced at random among those within such a group.
5
violence is “conditionally indiscriminate” within village and gender. While this assumption cannot be
proven correct on any observable data, it implies that observed pre-treatment characteristics should
be similarly distributed for those who are and are not injured during attacks, within village-gender
strata. I test this with a series of conditional balance tests (Section 4.1). The main results are then
given, using five different estimators to realize this conditioning strategy (Section 4). Finally, Section
5 discusses the risks of confounding.
3.1 Data
The data are drawn from a survey conducted between April and June of 2009 by the “Darfurian
Voices” team with support of the US Department of State. Informed consent was obtained from each
participant at the outset of each interview. A sample of 1,872 non-leadership individuals was collected
using a stratified random sampling method with geographic location (camp and block), gender, and
ethnicity as strata. The full survey was thus representative of adult refugees (18 years or older) from
Darfur, living in the 12 Darfurian refugee camps in eastern Chad at the time of sampling. The question
and research design posed in this paper, however, apply only to villagers who were present during the
time of village attack and thus subject to possibly being injured. Thus, the relevant sample is the 1,377
(74%) who reported leaving their village only when it was attacked. All analyses use this sample.4
Geography was the primary determinant of who immigrated from Darfur to Chad rather than
elsewhere; almost all Darfurian refugees in Chad hail from the western part of West Darfur. While
a large portion of families from those areas have come to and remained in the camps, some have
died, some have joined the armed movements, and some have gone elsewhere. These features of how
individuals “select-into-the-sample” certainly affect the inferences made here, raising two kinds of
concern. The first type of concern is how the effect of violence within this group might differ from the
effects in other groups. A second is whether these selection processes bias our estimates of the effect
of violence even within this group. I take this up extensively in Section 5.
3.2 Measurement and Key Variables
The key variable of interest is direct exposure to physical harm, coded as a binary variable Direct
Harm: “Have you suffered violence, or have you been physically maimed in an attack related to the
4Further details regarding this survey are available in the final report of the project, posted at http://www.
darfurianvoices.org. Detailed demographic characteristics from the original survey’s sample are reported at length
there, though I note that the sample used here is a subset of that sample as described above.
6
current conflict?”5In our sample, 41% report being directly injured or maimed. I examine the effects
of Direct Harm exclusively here principally due to identification concerns. Specifically, our identifying
claim—that for participants present when their village was attacked, the distribution of violence was as-
if random conditional on location and gender—does nothing to ensure the unconfoundedness of harms
relating to other people, such as the injury or death of neighbors or family members. For example, a
respondent could have family members who are more or less inclined to stay in the village, making
them more susceptible to injury. While this confound is avoided when speaking of the respondent’s
own experience because we know if she/he was present during the attack, we do not know if each family
member was present during the attack. Other benefits of using direct physical harm include that it is
relatively precise and objective compared to more diffuse measures of exposure, and the injury may
have a more salient, lasting impact on the lives of those who are injured, especially (but not only) if
there is a visible wound to remind them or others of their experiences, or if it produces a disability. Our
approach of focusing on only direct physical harm is admittedly narrow, and ignores other important
types of violence exposure other than direct physical harm.
Four separate outcome measures and a single score derived from them are considered. The first
three are binary variables indicating whether individuals reported believing it is possible to make peace
with former enemies (Peace Enemies), peace with individual Janjaweed fighters (Peace Janjaweed Indi-
viduals), and peace with the tribes from which the Janjaweed come (Peace Janjaweed Tribes). A fourth
question asked participants what punishment they felt would be appropriate for government soldiers
involved in the conflict (Execute Soldier). This is coded as a 1 when the answer was “execution,” and
0 for any other (lesser) punishment, and so points in the opposite direction to the previous three (the
more pro-peace answer now being the lower value). Note that this 0/1 coding also corresponds to a
median split.6Individuals’ answers to this question may reflect anger towards their perpetrator or a
desire for revenge, as opposed to a willingness to reconcile or live in peace with them. Responses to
this question nevertheless correlate well with the first three questions (beyond 0.27 for each pair).
For some analyses (such as the sensitivity analysis) it is useful to have a single summary measure,
rather than consider each outcome separately in each analysis. I use principal components analysis
to choose weights for summing these four measures into a single index. The outcomes are highly
correlated, with 52% of the variance loading onto the first component, which is used here as an index.
5This was asked near the end the survey to minimize priming effects. Because of the traumatic nature of these
experiences, participants were not asked to describe the violence they experienced.
6The survey also asked what people felt was the appropriate punishment for Janjaweed individuals involved in the
attack, but over 90% of respondents chose execution in each case.
7
As expected, the first three outcomes have similar weights and a common sign (.58, .40, .59), as each
asks about the possibility of peace with various groups. The last question, Execute Soldier, receives
a weight of similar magnitude but opposite sign (-0.40), also as expected, since higher values would
indicate “less-peacefulness.” To ease interpretation the resulting score, called Peace Index, is then
shifted and rescaled to have a minimum of 0 and maximum of 1. While this single factor does not
capture all of the variance of the four measures, it provides a reasonable weighted average useful as a
summary measure.
Both the “angry” and “weary” propositions make clear predictions for the directional effects of
violence on these outcomes. There is not yet a standardized and validated scale capturing these
constructs, and the measures here are certainly imperfect for capturing notions of pro-peacefulness/
weariness or pro-violence/ anger. Nevertheless, if direct harm is associated with more positive responses
on the first three questions regarding living together in peace with other groups, this would be consistent
with a weary or “pro-peace” response, and not with an “angry” response. The same is true if violence
is associated with a lower probability of endorsing the execution of government soldiers involved in the
conflict. As Peace Index has positive loadings for the first three questions and a negative for the latter,
a higher score for those who are directly harmed would be consistent with the pro-peace response and
a lower score would provide evidence against it.
3.3 Identification Assumption: Conditionally Indiscriminate Violence
The critical assumption required to identify the effect of violence on individuals is that among indi-
viduals of the same gender and from the same village, and who are present during an attack, their
chances of being physically harmed during that attack is unrelated to their attitudes. This can be
satisfied if violence is indiscriminate in its application, among individuals of a given gender from a
given village. I proceed by discussing this assumption in detail and its consistency with the observed
data. Section 5 discusses the consequences of violations of this assumption, and employes sensitivity
analyses to characterize how severely violated it would need to be to alter our conclusions.
Justifying this assumption requires characterizing how violence was perpetrated. During the height
of attacks in Darfur in 2003-2004, widespread violence against civilians was employed throughout
Darfur, including the state of West Darfur, from which almost all the survey respondents in this
study originate. The aim of these attacks was not to seek out rebel or political leaders. Rather, it
was to punish or destroy the communities thought to support the rebel groups, through violence and
forced displacement. Displacement of communities served a second purpose of incentivizing members of
8
the Janjaweed militia, whose tribes have long sought more reliable access to grazing lands, which they
could acquire by removing these groups. Villages are largely ethnically homogeneous, and the ethnicity
of a village was itself the basis for targeting that village, making individual-level targeting within it
unnecessary — and leading to charges of genocide, including in indictments by the International
Criminal Court.
Attacks on villages involved aerial bombardment and/or attacks by the Janjaweed militia. During
the bombing by government aircraft, injury occurred arguably at random. The bombings were often
as crude as pushing bombs, scrap metal, and barrels full of shrapnel out of aircraft, ruling out any
targeting based on political attitudes or other strategic considerations at the village level. The villages
also tend to be homogeneous in terms of the construction of housing within them, with little or no
variation in the quality of homes that would affect their ability to withstand bombings or provide hiding
spaces. In the ground attacks that often followed, the Janjaweed killed many men, and committed
widespread rape of women and girls. Conditionally on gender, the Janjaweed not only appeared to be
indiscriminate in their use of violence within each village, but also were unlikely to have any knowledge
of which individuals in the village were potentially more or less politically or militarily active. Evidence
is absent even that boys and men of fighting age were targeted, further emphasizing that the purpose
was not apparently to attack individuals thought to be a threat, but rather whole communities. These
types of attacks on whole villages were discrete events and did not generally lead to longer term
detention (e.g. abduction or forced portering), though other types of violence occurred outside these
village-level attacks, such as violence against women while collecting firewood outside of IDP camps.
Qualitative evidence also supports this picture of how the attacks occurred. In over 80 filmed and
transcribed interviews, the Darfurian Voices research team asked a range of open-ended questions that
included the nature of attacks on villages. The sample for these interviews was one of convenience,
heavily weighted towards those with leadership roles in the camp communities. Nevertheless, none of
the interviewees provided evidence suggesting that during village attacks the Janjaweed directed viol-
ence against particular types of individuals except by gender. Though there is evidence that Janjaweed
groups encountered on the roads and elsewhere interrogated individuals, during the village attacks the
common theme was that the Janjaweed would “kill everything.” As one respondent recounted, “The
government came with Antonovs (aircraft), and targeted everything that moved...If it moved, it was
bombed. It is the same thing, whether there are rebel groups (present) or not...They shoot everyone
when they see them from a distance...The government Antonovs survey the area from time to time to
see if there is anything moving and if it is a human or an animal...The government bombs from the sky
9
and the Janjaweed sweeps through and burns everything and loots the animals and spoils everything
that they cannot take.” Such statements look very similar to those collected by other organizations at
other times, such as those collected by Human Rights Watch (2004). Livestock and belongings were
often stolen (97% of respondents in our sample reported losing all or most of their livestock, crops,
and belongings), and villages were almost always burned to the ground. Further examination of these
interviews finds that those in the village, whether sleeping or attempting to flee, were subject to attack.
Even those fleeing to nearby hiding places were frequently pursued, and so ability to flee had a limited
effect.
4 Results
4.1 Covariate Balance
While anecdotal evidence, testimonials, and other information supports the “conditionally indiscrim-
inate” assumption, this claim also has implications for the observable data in the form of balance tests.
The type of balance test one would apply to a completely randomized experiment would test whether
the distribution of a series of pre-treatment covariate is the same for the treated and untreated groups.
The identification strategy implies the “as-if random” distribution of violence only within each village-
gender group. I therefore check balance only conditionally on village and gender, i.e. “conditional
balance”. To operationalize this, I stratify the sample by gender and then, within each, regress the
Direct Harm indicator on the pre-treatment covariates and village fixed effects. This tests whether on
covariates predict Direct Harm within village and gender. If exposure to Direct Harm is indeed unre-
lated to the distribution of a covariate (conditional on the others), its coefficient in this regression will
be zero in expectation. Covariates are included in this analysis if they are certain to be pre-treatment
(measured prior to the village attack or clearly not able to be altered by violence). In total these
include age; whether they were a farmer, herder, merchant, or trader in Darfur; their household size
in Darfur; and whether or not they had voted in the past. All results are shown with 95% confidence
intervals for reference, based on heteroscedasticity-robust standard errors. The analysis includes 486
unique villages, with no single village accounting for more than 7.1% of the sample.
Table 1 shows the results, indicating good conditional balance. The only covariate with a p-value of
less then 0.10 is Herder in Darfur: herders may be more likely to experience direct harm, conditional
on gender and village. Herders make up only 15% of the sample, and excluding them does not affect
the results reported below. Moreover, all pre-treatment covariates are not jointly predictive of who
experienced violence for either men (F= 1.235, p = 0.292) or women (F= 1.046, p = 0.391). I
10
therefore conclude that there is insufficient evidence to reject the null hypothesis of “no imbalance” on
observables, conditionally on village and gender.7
[Table 1]
4.2 Distributions of Treatment Probabilities
Another way to examine conditional balance is through the distribution of propensity scores, i.e. the
estimated probability that each individual is directly harmed. If the identification strategy is correct,
then after conditioning only on village and gender, the distribution of propensity score estimates should
look very similar for those actually harmed or not harmed. Conditioning on gender can be achieved by
separately plotting propensity scores. Adjusting for village can be achieved by a re-weighting procedure
that makes the distribution of villages the same for the harmed and unharmed.8Thus, any remaining
differences in the distribution of propensity to be harmed cannot be due to differences in village.
Simple propensity scores can be obtained by a logistic regression of Direct Harm on the pre-treatment
covariates – i.e. the fitted values from the models used in Table 1. The top row of Figure 1 shows the
gender-specific distributions of propensity scores without this re-weighting to adjust for village location.
The modeled probability of being harmed markedly differs for the harmed and unharmed, reflecting
that some villages experienced much more extensive violence than others (top row). This is to be
expected: targeting was based on village. However, once the untreated observations are re-weighted to
equalize the distribution of villages in these groups, the balance is extremely good, with very similar
distributions of propensity scores for the harmed and unharmed (bottom row).
[Figure 1]
4.3 Main Results
Estimating the effect of Direct Harm on each of the five outcomes requires a method of conditioning
on village and gender, with the option to further condition on the other pre-treatment covariates
to improve precision and adjust for chance imbalances. Because there are hundreds of villages and
7Note that while balance is traditionally tested as done here – construcintg null hypothesis of “no imbalance” and
seeking sufficient evidence to reject it – a more appropriate test may be an “equivalance test”, the sets imbalance of at
least a certain magnitude as the null, and puts the burden of evidence on rejecting that level of imbalance (Hartman and
Hidalgo 2018). Further, the sensitivity analyses presented in 5 formally examines how confounders as strongly related to
treatment as this or other covariates would alter our results.
8The weights used correspond to those one would use to construct an Average Treatment on the Treated (ATT)
estimate, deriving weights only based on the proportion of treated in each village. Specifically, for each directly harmed
participant, assign a weight of 1. For each participant not harmed, re-weight according to ωi=P(V illage=villagei|D=1)
P(V illage=villagei|D=0 ,
where villageiis the village from which participant ioriginates.
11
relatively few individuals from each, fully conditioning on village poses potential challenges. Here I use
three types of estimation strategies and five models in total to check for similar results across different
methodological choices: a matching approach; linear models with village and gender fixed effects; and
a similar fixed effects model but applied to data that have been pre-processed to achieve balance on
covariates, reducing model dependency.
First, observations can be matched on village and gender, together with the pre-treatment cov-
ariates. Matching is exact on village, gender, and indicators for being a herder in Darfur, being a
farmer in Darfur, and voting in the prior election. Age and household size (also when in Darfur) are
matched on as continuous variables, minimizing Mahalanobis distance. All matches are one-to-one.
Treatment effects are then computed, together with the Abadie-Imbens standard errors (Abadie and
Imbens 2006), as implemented in the Matching package for R(Sekhon 2011). Figure 2 shows results for
each of the five outcome variables. Although conditioning by matching is conceptually straightforward
and allows for non-parametric conditioning, it comes at a high cost because there are hundreds of
unique villages: from 1276 original individuals (529 of them harmed), matching essentially reduces the
dataset to 214 matched pairs, dropping roughly half the treated units and two thirds of the control
units. This motivates a variety of alternative estimators to ensure the robustness of results.
[Figure 2]
One alternative approach to account for village and gender is by including village and gender
indicators in a linear model. Such a model estimates an individual’s gender and village of origin as
if they have additive effects on the outcome, but avoids the severe loss of data imposed by matching
on village. The simplest such model includes indicators for each village and gender (Figure 2, “OLS-
short”).9Adding further covariates to the model is not required for identification purposes, but again
may improve precision or adjust for chance imbalances (Figure 2, “OLS-long”).
A final set of models seeks to account for village and gender through a similar regression with
village and gender indicators, but also seeks to reduce model dependency by first ensuring balance
in a pre-processing stage. I employ entropy balancing (Hainmueller 2012) to choose weights for the
unharmed individuals such that, after weighting, the means and variances of the covariates (other than
village and gender) are the same for harmed and unharmed individuals. I then employ these weights
in regressions with village and gender indicators to complete the required conditioning. Again, this is
done with (a) a “short” outcome model to achieve identification (gender and village indicators); and
9For the binary outcomes, this is a linear probability model. Accordingly, all standard errors are heteroscedasticity
robust.
12
(b) a “long” specification in which the covariates are (re-)included in the regression stage for additional
robustness (Figure 2, “ebal-short” and “ebal-long”).
Results are remarkably stable across models. All five estimation procedures find that directly
harmed individuals are approximately 10% (percentage points) more likely to say it is possible to live
in peace with former enemies, to live in peace with individual members of the Janjaweed, or to live
in peace with the tribes from which the Janjaweed were drawn. Under every model, results on these
three outcomes fall in the 8-12% range, and all 95% confidence intervals widely exclude zero. These
are substantively large effects given the overall averages for these outcomes, ranging from 17% to 39%.
Each model finds that those directly harmed are also 9-10% less likely to report that Government of
Sudan soldiers involved in the attacks should be executed. Again all 95% confidence intervals exclude
zero. Finally, Peace Index (the summary score created by a weighted average of these four), is .09 to
0.10 units higher among those directly harmed, under all five modeling approaches. This variable is no
longer binary, but has a similar scale to the other outcomes (minimum of 0, maximum of 1, and mean
of 0.32), making this a substantively large difference. These estimates are approximately the same
size as those on each individual outcome, with somewhat smaller standard errors, suggesting that this
summary score measures a similar construct as each outcome but reduces measurement error through
averaging. Collectively this evidence is consistent with what is expected under an on-average “weary”
reaction to direct harm.
5 Robustness and Sensitivity
As a quasi-experimental study, further validity checks and an examination of possible alternative
explanations are in order before proceeding to interpretation.
5.1 Robustness to Confounders
This identification strategy requires that violence was indiscriminate among people from the same
village and gender. While the balance tests show the observed data to be consistent with this claim, such
a claim cannot be definitely proven on observable data. Here I argue that confounding by unobservables
is unlikely to be responsible for these results through (1) discussing the likely direction of bias; (2) a
placebo test using an alternate outcome that should not be affected; and (3) sensitivity analyses.
Expected direction of bias. Perhaps the most obvious and worrying source of bias is pre-existing
attitudes that might drive both risk of exposure to harm and answers to questions about peace.
13
Specifically, we might expect that those who are more anti-government, more bellicose, or otherwise
more interested in supporting the rebellion may be more likely to put themselves in harm’s way by
rushing into the fight, increasing their chances of exposure to violence. We would expect this group to
be the less peaceable in their responses. Hence the bias expected here (and in prior work on this topic)
would be towards observing a less pro-peace response. That we see the opposite is thus reassuring from
the perspective of our confidence that the result is not due to confounding of this most expected kind.
It is less obvious how those who are more pre-disposed to peaceful attitudes could be made more likely
to experience violence in order to generate bias in the opposite direction — particularly given that we
only consider those who were present in their village during the attack and the lack of targeting within
village-gender strata. Nevertheless, biases in either direction cannot be ruled out.
Placebo test. Using the same analyses as above, I also find that those directly harmed are 9-10
percentage points more likely (p≤0.015) to say they would vote in future elections in Darfur, echoing
prior work on violence and political engagement (Blattman 2009; Bateson 2012). This suggests a useful
placebo test: despite this relationship to reported future voting intention, under the identification
strategy, after conditioning on village and gender we should find no relationship between direct harm
and whether people reportedly voted in the past (Past Voted). Using Past Voted as a (placebo)
outcome, I indeed find that it is not significantly related to direct harm (coefficient of 4-5%, p≥0.26
from OLS-short OLS-long models.)
Formal sensitivity analysis
Third, rather than qualitatively debate whether the bias is exactly zero, we can more productively
discuss “how strong confounding would need to be to substantively alter our conclusions” through a
sensitivity analysis following Cinelli and Hazlett (2018).10 Table 2 shows the regression results for the
OLS-long model described above with Peace Index as the outcome, augmented by several quantities
that describe the sensitivity of the result to unobserved confounding.
[Table 2 ]
On Table 2, the Robustness Value (RV ) of 13.9% means that: if confounding explains less than
13.9% of the residual variance in exposure (Direct Harm), and less than 13.9% of the residual variance
in the outcome (Peace Index ), then confounding cannot be strong enough to overturn or “explain
10This approach can be implemented in Rusing the sensemakr package (Cinelli and Hazlett 2019).
14
away all of” the effect estimate. Similarly, the RVα=0.05 of 7.6% tells us that confounding would have
to explain more than 7.6% of the residual variance in exposure and the outcome in order for the
unbiased estimate to lose statistical significance at the 0.05 level.11 These results indicate that not
“just any confounder” we may think of would alter our conclusion; rather, confounding must arguably
approach the strength described here. To examine arguments about confounders that unequally relate
to exposure and harm, we can consult contour plots such as Figure 3. This shows how hypothetical
confounding, indexed by its strength of association with Direct Harm (horizontal axis) and with Peace
Index (vertical axis) would change the effect estimate.
To aid interpretation, we can further ask how much stronger confounding would have to be than
some important observed covariate in order to change the result. The lower-right corner of Table 2 tells
us that if Female is assumed to be “stronger” than confounding (by explaining at least as much residual
variance in both exposure and outcome as does the confounder), then we can formally determine that
confounding can explain at most 12% of residual variation in Peace Index (R2
Y∼Z|X= 12%), and at
most 1% of residual variation in Direct Harm (R2
D∼Z|X= 1%). We can see how such a confounder
would alter our conclusion in Figure 3, which shows the effect estimate after adjusting for a confounder
“as strong as female” (1x female). As this has little impact on the estimate, I also show what would
happen if confounding was “twice as strong as” female (2x female), or “three times as strong as” female
(3x female). The effect remains positive in each case. Figure 4 shows similar analyses, but plotting the
value of the t-statistic adjusted for each level of proposed confounding. This shows that if confounding
was “twice as strong as Female,” the result would remain statistically significant (t= 2.60), but at
confounding three times as strong as Female, the (adjusted) estimate would no longer be distinguishable
from zero at the α= 0.05 level, with t= 1.63.
This is particularly informative because Female is a “strong” covariate: The bombs could not be
targeted at all, and when the Janjaweed attacked villages, it is difficult to imagine any visually apparent
characteristics that drove targeting of harm more than Female. An assumption that confounding is no
stronger than Female thus sets the bar high. In terms of its explanatory power over the outcome (Peace
Index ), Female also turns out to be a powerful variable, with a t-statistic of over 9 and explaining far
more variation than any other observed covariate. That said, unlike the targeting argument, there is
not a clear theoretical reason to believe that it is stronger (explains more of the residual variation)
than any confounder. Nevertheless, to say that “confounding would have to be more than twice as
11We can simply take the square root of these RV values for users who are more familiar with thinking in terms of
partial correlations rather than this partial variance explained (R2) scale. For example, to reduce the estimate to statistical
insignificance, confounding must have a partial correlation with both exposure and outcome of at least √7.6% = 28%.
15
strong as Female in order to reduce the result below statistical significance” illuminates the types of
confounding that would be problematic. Finally, even if confounding explains 100% of the residual
variation in the outcome, a confounder that explains no more of the residual variation in expoure than
Female cannot possibly overturn the result.12
[Figure 3]
[Figure 4]
5.2 Spillover Effects
We cannot reasonably assume that one individuals’ exposure to violence has no effect on the outcome
of other individuals, as commonly required under the “Stable Unit Treatment Value Assumption”,
or SUTVA (Rubin 1980). One possibility is that when a person experiences direct violence, those
around her but who do not experience it receive, on average, a mitigated effect in the same direction.
This would bias the estimated effect toward zero. “Negative” spillover is also possible: when person j
experiences violence, its effect on (an untreated) person imay be opposite in direction to the effect on
j. For example, those who are harmed may become more pro-peace, but those not harmed experience
something akin to survivor’s guilt and become more vocally militant or anti-peace. That said, the
difference between the groups in such a case would still describe an important causal effect of violence—
one that derives in part from the effect on the unharmed.
5.3 Correlated Measurement Error
Another potential threat is that errors in reporting of direct harm and the outcome may be correlated,
causing bias. For example, some respondents may seek to show enumerators that they both (a) have
suffered and are thus in need of support from donors, and (b) are of a pacific nature, more likely
to attract donors to continue supporting the camps. This seems unlikely to explain the observed
effect: if strategic misrepresentation of this type was driving the effect, we would also expect to see
similar (false) effects for the indirect forms of violence, such as the loss of family members. The same
individuals would be expected to over-report losses on these measures, while also reporting being more
conciliatory, again confounding the relationship between Direct Harm and attitudes. Those analyses
12Specifically, another quantity given on Table 2 is the R2
Y∼D|Xof 2.2%, which tells us that even if 100% of the residual
outcome variation is explained by confounding, such confounding would have to explain 2.2% of residual variation in
exposure to Direct Harm in order to account for the effect estimate. By contrast we know from the above that confounding
as strong as Female can only explain 1% of the residual variation in Direct Harm.
16
show no measurable effect of indirect forms of exposure on attitudes, though they are also based on a
low level of variation and thus have low statistical power.
5.4 Survivorship and Selection into Refugee Camps
“Selection-into-the-sample” can pose a challenge depending upon its form and relationship to both
Direct Harm and attitudes.
A first concern is that some or many of the injured may have died. However, the chances of a
harmed individual surviving their injury is plausibly unrelated to their attitudes. Thus, the harmed
individuals present in the sample are not likely to be more vengeful or more pacific than the harmed
individuals who did not survive, and no bias results.
By contrast, bias could result if among those who are harmed, the most vengeful or pro-violence
among them never came to the camps, or have since left the camps, perhaps after receiving medical
care. To examine this possibility, note that a process that would selectively drive the“vengeful-and-
harmed” back into the fight (and out of our sample) would act far more powerfully on men of fighting
age, because in this context, few women or elderly participate directly in the armed opposition groups.
If such a process drove the results, we would see the apparent effect most strongly among young men,
but should see little or no apparent effect among women or the elderly who are far less likely to join
the opposition. This is not the case. Among women, those directly harmed score 0.08 points higher
on Peace Index (using OLS-short and OLS-long, both with p < 0.07). While not quite significant
at conventional levels, the sample size is roughly half that of previous analyses. Among individuals
over 50 years old, the effect of harm on Peace Index is even stronger than in the full sample, at 0.14
(OLS-short and OLS-long, both with p < 0.001). Hence, the effect estimate observed is not apparently
due to this particular form of selective missingness from the sample.
6 Discussion
Understanding whether violence experienced by civilians generates more “angry” and pro-violence, or
more “weary” and pro-peace responses has important implications for the continuation, termination,
and recurrence of civil conflicts. Yet, confounding concerns have long complicated efforts to answer
this question. This study employs a quasi-experimental strategy to estimate the effect of being injured
or maimed by violence on attitudes toward peace, among Darfurian refugees in eastern Chad. The
findings are consistent not with an “angry” or pro-violence response, but rather with a “weary” or
pro-peace response: Those exposed to direct violence are approximately 10 percentage points more
17
likely to report the pro-peace answer on questions regarding optimism for peace and the punishment
of former enemies. Although these results may at first seem counter-intuitive, they are consistent
with recent works that have observationally studied the relationship between exposure to violence and
attitudes toward peace (Tellez 2018; Krause 2017; Bakke et al. 2009), while providing a micro-level
foundation for prior work on war-weariness.
6.1 Generalizability
The inferences made here apply to the group studied and cannot speak to how civilians elsewhere in
Darfur, much less other conflicts, respond to violence. Further, the estimate here isolates only the
additional effect of being physically harmed, above and beyond all other harms faced by individuals
and communities. When forming expectations about the effects of violence in other cases, two major
conditions of the current study may be of theoretical relevance. The civilians studied here have fled
the conflict zone, and faced violnece that they knew to be targeted at groups, rathern than selective
violence based on individual loyalties or behaviors. These features break from the framework civilians
who are captive in the conflict zone, deciding their wartime loyatlies under the shadow of selective
violence as developed in Kalyvas (2006).
The elapsed time since violence occurred is another important consideration. Would the effect be
in the “weary” direction shortly after violence occurs, and would this effect persist over decades or
generations? These are theoretically important considerations that the present study cannot speak to
them. Rather, the research agenda for the future could fruitfully aim to better understand the entire
time-course of responses to violence.
6.2 Possible Mechanisms
This study seeks to make a credible claim as to the effect of exposure to direct harm on attitudes toward
peace in one context, and can provide only suggestive evidence for or against proposed mechanisms
for that effecy. Nevertheless, the theories reviewed above provide a number of possible explanations,
and evidence from this paper points suggests practical directions for a research agenda that could
distinguish among them. The first explanation is simply that those subjected to direct violence ex-
perience heightened costs of conflict, making further conflict less appealing, and making peace more
precious. Faced with the memories and pain of their losses, these individuals would prefer peace over
the continuation or recurrence of violence.
Second, post-traumatic growth theory (Tedeschi et al. 1998; Tedeschi and Calhoun 2004) posits
18
that increased altruism and social engagement are more common outcomes than social alienation or
psychiatric illness. This appears to be a plausible. That said, it is not obvious as to why “personal
growth” should necessarily imply more pacific attitudes, particularly in cultural contexts where a desire
to protect one’s community (including through violence) may be considered a virtue.
A third possible explanation involves an assumption that individuals are socially expected to show
anger or a desire for revenge in response to offenses (as in the “culture of honor” theory Nisbett
and Cohen 1996), but that some individuals – those who are injured – can earn an exemption to
this requirement, and choose to speak out in favor of peace. I refer to this as the “culture of honor
exemption” hypothesis. Though complicated, this proposal was inspired by qualitative experiences
while collecting data in these refugee camps. Those who were injured frequently nominated themselves
as spokespeople, approaching the research team, giving evidence of their injuries, and telling us their
perspective and very often their interest in seeing a peaceful resolution.13 This explanation, however,
leaves unanswered (a) why individuals who are injured would be given the hypothesized exemption
from norms calling for reciprocal violence; and (b) why harmed individuals would be inclined to use
this exemption as an opportunity to become more pro-peace.
7 Conclusions
When exposed to violence, civilians may become more supportive of further violence, or more strongly
desire and support calls for peace. These two opposing responses have very different implications
for how we expect violence to influence civil war escalation and termination, and the prospects for
post-conflict stability and cooperation. This study employs a quasi-experimental design in the case
of Darfur to study whether exposure to direct harm causes individuals to predominately adopt more
pro-peace or more pro-violence attitudes. On average, directly harmed individuals are found to be
more supportive of peace and less interested in executing their enemies, consistent with theories and
accounts of “war-weariness”. One consequence of this finding is that even where violence against
civilians has been extreme, there can remain constituencies that seek peace and would support leaders
calling for it. This finding argues against views that violence necessarily begets violence, leaving only
military victory or population separation as viable options to end the conflict. Rather, if sufficient
proportions of civilians crave peace despite—or because of—their experiences with violence, political
settlements, security arrangements, and disarmament may be viable options. Moreover, individuals
13This was unlikely simply an effort to show outsiders “what they want to see,” as other groups of refugees were
sometimes noted to promote more vengeful attitudes. See Hastrup (2013) for examples from the same camps.
19
directly and severely harmed by violence may no be spoilers, but rather valuable participants in such
processes.
Considerable room remains for this research agenda and to examine the mechanisms proposed
above. Regarding measurement challenges, it would be useful to develop and standardize survey
instruments that explore a greater variety of dimensions on which civilian attitudes toward peace,
justice, and reconciliation may vary. It would also be preferable to examine behavioral outcomes
that indicate preferences for peace or violence rather than rely on self-reported attitudinal measures.
Second, while the focus here was narrowly on identification and estimation of the effect of violence,
arbitrating among possible mechanisms is an important next step. To test mechanisms proposed
here, research could fruitfully examine whether survivors of direct harm see the costs of continued
conflict as being starker than others do, and whether communities view victims of direct violence as
having greater authority to speak and or an exemption from norms requiring support for retribution.
Further examining the relationship between violence and post-traumatic growth, and the connection
between post-traumatic growth and pacific attitudes, would also be valuable. Third, further work on
the question of how exposure to violence relates to attitudes toward peace is needed across a diverse
range of conflicts and contexts, for replication purposes as well as to determine the conditions upon
which these effects depend.
20
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Table 1: Multivariate balance test conditional on village and gender
Female Male
Odds Ratio Odds Ratio
(p-val) (p-val)
Age 0.996 0.998
(0.759) (0.293)
Farmer in Darfur 1.349 0.882
(0.581) (0.743)
Herder in Darfur 2.163 2.631
(0.135) (0.047)
Pastvoted 1.77 0.959
(0.19) (0.905)
Household size 1.039 0.981
in Darfur (0.194) (0.483)
Joint F-stat (Wald) 1.046 1.235
Joint p 0.391 0.292
N 582 694
Note: Conditional balance test to determine whether observed, pre-treatment covariates are associated with
Direct Harm conditionally on village and gender. Logistic regression of Direct Harm on village fixed effects
and all pre-treatment covariates, separately for men and for women. Odds ratios are shown. The results show
good balance overall, with odds ratios near to one, and the only marginally significant relationship being on
the indicator for individuals who were herders in Darfur. Wald tests fail to reject the null hypothesis that all
coefficients (except those on the village fixed effects) are zero.
Table 2: Regression results with sensitivity statistics
Outcome: Peace Index
Treatment: Est. SE t-value R2
Y∼D|XRV RVα=0.05
Directly Harmed 0.097 0.023 4.18 2.2% 13.9% 7.6%
df = 783, Bound (Zas strong as Female): R2
Y∼Z|X,D = 12%, R2
D∼Z|X= 1%
Note: Results of “OLS-long” regression of the outcome (Peace Index ) on the exposure (Direct Harm) together
with pre-treatment covariates and village and gender fixed effects. The usual regression results are augmented
with the sensitivity statistics RV ,RVα=0.05, and R2
Y∼Z|X,D, described in the text. The bottom row of the
table also shows bounds on how strongly confounding can relate to Direct Harm and Peace Index, under the
assumption that confounding explains no more of the residual variance in these than that explained by the
observed covariate Female.
24
Figure 1: Propensity score distributions for the harmed and unharmed
0.0 0.5 1.0
01234
Pr(Physical Harm)
Density
Physically Harmed
Not Physically Harmed
(a) Female, unweighted
0.0 0.2 0.4 0.6 0.8 1.0 1.2
01234
Pr(Physical Harm)
Density
Physically Harmed
Not Physically Harmed
(b) Male, unweighted
0.0 0.5 1.0
0.0 0.5 1.0 1.5 2.0 2.5 3.0
Pr(Physical Harm)
Density
Physically Harmed
Not Physically Harmed
(c) Female, weighted on village
0.0 0.2 0.4 0.6 0.8 1.0 1.2
0.0 0.5 1.0 1.5 2.0 2.5 3.0
Pr(Physical Harm)
Density
Physically Harmed
Not Physically Harmed
(d) Male, weighted on village
Note: Propensity scores for harmed and unharmed individuals, using same model of pre-treatment covariates
used in multivariate balance testing. Top: Without conditioning on village, the propensity score model can
distinguish between those likely to be harmed and those who are not on the basis of their covariates. Bottom : The
same propensity scores for harmed and unharmed individuals, after weighting the data so that the distribution
of villages is the same for the harmed and unharmed.
25
Figure 2: Estimated effect of exposure to direct harm on attitudes under five models
●
Peace with
Former Enemies
(mean=0.388)
●
Peace with
Janjaweed Individ.
(mean=0.172)
●
Peace with
Janjaweed Tribes
(mean=0.328)
●
Should Execute
Government Soldiers
(mean=0.622)
●
Peace Factor
(mean=0.324)
−0.2 −0.1 0.0 0.1 0.2 0.3
Effect of Physical Harm on Positive Response
●Match
OLS−short
OLS−long
Ebal−short
Ebal−long
Note: Estimated effect of Direct Harm on various outcomes, with 95% confidence intervals. Five modeling
approaches are shown: matching on the key conditioning variables (village and gender) as well as pre-treatment
covariates (Match); a minimal OLS model including village and gender fixed effects (OLS-short); a fixed effects
model and including the remaining pre-treatment covariates (OLS-long); and a model that pre-processes the
data using entropy balancing on pre-treatment covariates other than village, followed by the short-OLS and
long-OLS models using the derived weights (Ebal-short, Ebal-long). All results show that direct harm moves
attitudes in the “pro-peace” direction.
26
Figure 3: Sensitivity of point estimate with bounds
Hypothetical partial R2 of unobserved confounder(s) with the treatment
Hypothetical partial R2 of unobserved confounder(s) with the outcome
−0.3
−0.28
−0.26
−0.24
−0.22
−0.2
−0.18
−0.16
−0.14
−0.12
−0.1
−0.08
−0.06
−0.04
−0.02
0.02
0.04
0.06
0.08
0.0 0.1 0.2 0.3 0.4
0.0 0.1 0.2 0.3 0.4
0
Unadjusted
(0.097)
1x female
(0.08)
2x female
(0.05)
3x female
(0.03)
Note: Sensitivity analysis including benchmark bounds, derived from claims that confounding is once, twice,
or three times “stronger” than Female in explaining residual variation in Direct Harm and Peace Index. The
horizontal axis shows hypothetical values for the percentage of the residual variance of the treatment explained
by the confounder. The vertical axis shows hypothetical values for the percentage of the residual variance of
the outcome explained by the confounder. The contour levels represent the adjusted estimates of the treatment
effect. The bound points (diamonds) show the partial R2of the unobserved confounder under the assumption
that it is ktimes “as strong” as the observed covariate Female. Their placement thus shows the maximum bias
caused by confounding, under each assumption on k(1, 2, or 3). The point estimate of the treatment effect
remains positive for a confounder once, twice, or three times as strong as Female.
27
Figure 4: Sensitivity of t-statistic with bounds
Hypothetical partial R2 of unobserved confounder(s) with the treatment
Hypothetical partial R2 of unobserved confounder(s) with the outcome
−13
−12
−11
−10
−9
−8
−7
−6
−5
−4
−3
−2
−1
0
1
2
3
4
5
0.0 0.1 0.2 0.3 0.4
0.0 0.1 0.2 0.3 0.4
1.96
Unadjusted
(4.2)
1x female
(3.44)
2x female
(2.6)
3x female
(1.63)
Note: Sensitivity analysis of the t-value including benchmark bounds. Axes are defined as before (see Figure
3), but contour levels now show the adjusted t statistics of the treatment effect for given pairs of partial R2of
the confounder. The reference points again show the bounds on the strength of the unobserved confounder if it
were once, twice, or three times “as strong” as Female. The t-value remains well above the usual critical value
of 2 for a confounder twice as strong as Female, then falls below.
28
