## Abstract

We estimate the impact of Kenya's postelection crisis on individual risk preferences. The crisis interrupted a longitudinal survey of more than five thousand Kenyan youth, creating plausibly exogenous variation in exposure to civil conflict prior to the survey. Our results indicate that the postelection crisis sharply increased individual risk aversion. Immediately after the crisis, the fraction of subjects displaying extreme risk aversion increased by more than 80%. Findings remain robust when we use an IV estimation strategy that exploits random assignment of respondents to waves of surveying. The crisis also affected trust, social capital, and beliefs about the economy.

## I.  Introduction

ARMED conflict is a source of untold human suffering. Since 1989, more than 1 million people have been killed in civil and interstate conflicts (Pettersson & Wallensteen, 2015). The majority of these episodes are civil wars in low- and middle-income countries. Because the scourge of war falls disproportionately on the poorest nations, armed conflict also perpetuates disparities in human and economic development among the living.

The short-term costs of civil conflict are obvious: in addition to the lives lost, violence destroys physical capital and deters investment. There is also evidence that war and violence limit the accumulation of human capital (Blattman & Annan, 2010) and erode trust (Nunn & Wantchekon, 2011). This has led some scholars to refer to civil war as “development in reverse” (Collier et al., 2003). Yet though the short-term human and economic costs of conflict are indisputable, many conflict-affected countries—Rwanda and Uganda, for example—have experienced extremely rapid growth in the wake of civil war, and a number of recent papers have challenged the notion that conflict leads to slower growth and development over the long term (cf. Miguel & Roland, 2011). In fact, several studies have found that exposure to civil conflict increases political engagement (Bellows & Miguel, 2009; Blattman, 2009), enhances cooperation and prosociality (Voors et al., 2012, Bauer et al., 2014, 2016), and makes people more willing to bear profitable risks (Voors et al., 2012; Callen et al., 2014).

These studies share a common empirical approach. First, they take seriously the idea that exposure to conflict is endogenous, and they employ a variety of strategies designed to isolate plausibly exogenous variation in victimization and involvement in violence. Second, given their focus on within-conflict variation in exposure and victimization, these papers empirically frame civilians who lived through civil war but were not victimized (or were less exposed to violence) as a comparison group.1 This strategy contributes to the credibility of the estimated treatment effects but has an obvious drawback: it cannot be used to assess the overall impact of conflict unless one assumes that violence has no impact on the relatively less victimized (who serve as the comparison group). If everyone who lives through a period of conflict, regardless of their victim status, is affected, estimates of the marginal impact of greater conflict exposure may present a biased assessment of the overall social cost of violence. Moreover, since civil conflict typically involves a contest for control of a state government, some increase in political and economic uncertainty almost always arises and affects everyone. Empirical approaches that frame less exposed citizens as the comparison group cannot capture the impacts of these macrolevel shocks. Thus, to capture the overall impacts of civil conflict on society, an alternative empirical approach is required.

In this paper, we estimate the impact of a specific episode of civil conflict, Kenya's postelection crisis, on the risk preferences of a broad sample of young adults who lived through it. The postelection crisis was a months-long period of protests, rioting, and ethnic violence that began immediately after a disputed presidential election. The election, in which Raila Odinga challenged incumbent Mwai Kibaki, took place on December 27, 2007. Amid allegations of electoral fraud by observers and after three days of uncertainty following the national polls, the incumbent president was both declared the winner and sworn into office on December 30, 2007. Ethnic tensions rose, and rioting ensued. The following two months of civil conflict left more than a thousand people dead and hundreds of thousands more internally displaced. The crisis ended when the two candidates signed a power-sharing agreement on February 28, 2008.2

We estimate the impact of Kenya's postelection crisis on individual risk preferences, which we measure using lottery choice questions embedded in a longitudinal survey.3 The Kenyan Life Panel Survey is a survey of more than 5,000 young adults who were enrolled in rural primary schools in 1998. The second round of the survey (KLPS2) was administered between August 2007 and December 2009, with 1,179 respondents (23.3%) interviewed prior to the crisis and the remainder surveyed after experiencing the period of civil conflict. Thus, Kenya's postelection crisis interacted with the timing of the survey to create a natural experiment in exposure to conflict.

We employ two complementary identification strategies to estimate the impact of the crisis on risk aversion. First, we estimate the impact of the crisis in straightforward linear and nonlinear frameworks, using several strategies to control for any time trends or seasonal shocks. Second, we exploit the fact that survey respondents were randomly assigned to one of two waves of interviews; Kenya's election crisis interrupted the first wave of surveys, allowing us to instrument for being surveyed after experiencing the crisis using the randomly assigned survey waves. Both approaches yield similar results. We find that Kenya's postelection crisis had a large and significant impact on individual risk aversion. Specifically, the crisis led to a 10.9 percentage point increase in the likelihood that a subject always chose the safest, lowest-expected-value alternative (i.e., lottery) available; this effect constitutes an 81.7% increase in the rate of extreme risk aversion. We also observe a 5.6 percentage point (or 26.1%) decrease in the fraction of subjects classified as either risk neutral or risk loving. Such substantial impacts highlight an important channel through which civil conflict might affect growth and development: increased risk aversion might lead individuals in postconflict settings to avoid high-risk, high-return activities (e.g., entrepreneurship) that contribute to economic growth.

One important question is whether the primary channel through which conflict affects risk tolerance is economic. The crisis may have lowered real incomes, for example, by driving up prices or reducing employment. If that were the case, we might attribute to the postelection crisis itself the impacts of the resulting economic shock. In fact, while we find that the postelection crisis had a significant negative impact on beliefs about the economy, it did not have a negative impact on the wages or job prospects of the young adults in our survey. Instead, we find a modest positive impact on the likelihood of employment. In addition, though prices increased during the crisis, our results are robust to the inclusion of the inflation rate as a control variable, suggesting that observed effects are not driven by price changes. Thus, our results do not seem to be driven by purely economic phenomena such as changes in wages or prices (though we cannot fully rule out the possibility that the crisis made young adults unduly pessimistic about their future incomes). However, we do find that the crisis damaged the fabric of Kenyan society, even though the areas that we study were not the most directly affected. The crisis led to significant declines in participation in community groups and generalized trust, particularly the extent to which respondents trust members of other ethnic groups. Thus, the postelection violence appears to have affected Kenyan society through several channels, but our results suggest that it primarily (and directly) affected individual values, beliefs, and preferences—observed effects cannot be explained by changes in prices and wages.

The key contribution of our study is that we are able to estimate the impact of civil conflict on the risk preferences of those less exposed to violence, as opposed to the specific (marginal) effect of being more exposed to violence relative to a comparison group that also lived through a conflict. Like all other Kenyans, KLPS2 respondents experienced a period of acute anxiety about the political and economic future of their country. Moreover, they experienced the violence firsthand, though relatively few were themselves victims. Ninety-four percent indicated that they were “worried” about their own safety and the safety of their family members during the crisis, and 76% were unable to procure basic necessities because it was unsafe to travel from their home to the nearest market. In addition, 8.9% of respondents were victimized in some way: either they were assaulted, a household member was assaulted, they were robbed, or they had property burned during the crisis. Given the short duration of the postelection violence (roughly two months), it is clear that these numbers indicate a relatively high risk of being victimized. However, no KLPS2 respondent was killed, and the majority of KLPS2 respondents spent the crisis in a rural district that experienced widespread clashes, rioting, and looting, but recorded only nine conflict-related deaths (Waki, 2008). Thus, KLPS2 respondents experienced the conflict but were not, by and large, among the most affected Kenyans; they therefore provide an important window into the impacts of civil conflicts on the preferences of nonvictims.

Of course, our empirical approach is not without drawbacks. Importantly, we cannot separate the effects of the violence (and the risk of violence) from other aspects of the postelection crisis—for example, political uncertainty and the possibility of future violence. We argue that political uncertainty, almost by definition, is an attendant feature of civil conflict. In many studies of the impact of violence on those more exposed within a conflict, these aggregate impacts are differenced out. Estimating the overall impact of civil conflict, including the effects of the inherent political and economic uncertainty, is therefore an important next step in the literature.

Our results differ from several recent studies. For example, Voors et al. (2012) find that greater exposure to violence leads to an increase in risk-seeking behavior, while Callen et al. (2014) find that priming subjects with recollections of violent events increases their risk tolerance, particularly in situations where no certain outcomes are available. However, these differing results can be reconciled by the difference in estimands—for example, if those who narrowly escape being victimized become more risk averse or the political uncertainty inherent in civil conflict makes everyone more risk averse.4 Our aim in this paper is to estimate the overall impact of violence; doing so, we may not find the same effect.5 Understanding these overall impacts is of critical importance as we seek to characterize the ways that conflict may change a country's overall growth trajectory.

This paper contributes to several strands of literature. First, most obviously, we add to the evidence on the impacts of conflict. This literature has expanded rapidly in recent years as increasingly high-quality microdata sets from postconflict settings have become available. Humphreys and Weinstein (2006), Bellows and Miguel (2009), and Blattman and Annan (2010) made prominent early contributions. Blattman and Miguel (2010) and Bauer et al. (2016) provide detailed discussions of the literature.

Second, we contribute to a growing body of evidence that individual preferences are shaped by life experiences. For example, Malmendier and Nagel (2011) and Fisman, Jakiela, and Kariv (2015) show that preferences are affected by exposure to economic downturns, while Cameron and Shah (2015) and Hanaoka, Shigeoka, and Watanabe (2018) document the effects of natural disasters on preferences. Several papers (e.g., Voors et al., 2012) have estimated the marginal impact of greater conflict exposure on the preferences of those most affected. Estimates of the overall impact of civil conflict on the preferences of the population are relatively rare, but our results resonate with recent work by Brown et al. (2015), who find that spikes in drug-related violence increase risk aversion among those not directly involved.6

Finally, our study contributes to the growing body of evidence documenting the predictive power of laboratory-style measures of individual preferences. Numerous studies document the explanatory power of experimental measures of risk, time, and social preferences. For example, Liu (2013) shows that experimental measures of risk preferences predict the crop choice and investment decisions of Chinese farmers.7 To date, the majority of work linking choices in decision experiments to behavior outside the lab has used incentivized measures of individual preferences.8 The evidence suggests that the use of incentives shifts individual responses toward greater risk aversion (Camerer & Hogarth, 1999; Holt & Laury, 2002), leading many to question the broad applicability of hypothetical approaches to risk preference elicitation. We contribute to this literature by demonstrating that hypothetical measures of risk preferences predict real-world behaviors in an internally consistent way. In particular, our measure of risk preferences is associated with real-world behaviors that involve risk: migration and entrepreneurship.

The rest of this paper is organized as follows. In section II, we describe the KLPS2 data collection effort and Kenya's postelection crisis. In section III, we describe our measure of risk preferences and assess the extent to which our hypothetical lottery choice questions predict behaviors likely to depend on risk aversion. In section IV, we explain our analytic approach and present our main results. Section V concludes.

## II.  Research Design

### A.  The Kenyan Life Panel Survey

We measure the risk preferences of a large and heterogeneous sample of young Kenyans by embedding a series of nonincentivized decision problems in the second round of the Kenyan Life Panel Survey (KLPS2), which was administered to more than 5,000 individuals enrolled in primary schools in Kenya's Western Province in the late 1990s.9 KLPS2 was administered in person, through one-on-one interviews, between August 2007 and December 2009. The survey covers a broad range of topics including educational attainment, labor market and entrepreneurial activities, household composition, migration, and fertility. Our sample includes 5,047 Kenyan youth aged 14 to 31. Summary statistics characterizing our respondents are reported in online appendix table A2.

### B.  Kenya's Postelection Crisis

The 2008 postelection crisis was a period of violence and political instability following the Kenyan presidential election of December 27, 2007. The two leading candidates in the election were Raila Odinga (the son of Kenya's first vice president) and the incumbent president, Mwai Kibaki (himself a former vice president). For several months preceding the election, opinion polls placed the opposition candidate, Odinga, ahead of Kibaki (Munene & Otieno, 2007). As election day neared, the polling gap between Odinga and Kibaki narrowed to what in some polls appeared to be a statistical dead heat (Agina, 2007; Otieno, 2007; World Bank, 2008). At the time of the election, both international observers and members of the opposition made allegations of electoral irregularities; however, after a few days, Kibaki was declared the winner and sworn into office (BBC, 2007; McCrummen, 2007; Waki, 2008). Opposition supporters organized protests; rioting and violent clashes with police ensued, and the violence soon escalated and took on a strong ethnic dimension (Waki, 2008; World Bank, 2010; Van Praag, 2010). By the time Kibaki and Odinga signed a power-sharing agreement at the end of February 2008, more than one thousand people had been killed and hundreds of thousands had been internally displaced (BBC, 2008a, 2008b).

All KLPS2 respondents were residing in Busia District, in Kenya's Western Province near the Ugandan border, in 1998; 73% were still living in Busia District at the time of the KLPS2 survey, and many others happened to be there during the postelection crisis (because they had returned to their family homes to celebrate the Christmas holiday or to vote). As a result, most were spared the worst of the postelection violence. Though protests, riots, and assaults took place throughout Kenya, the most affected areas were Rift Valley Province and the more urban districts across the country. According to the official report of the Commission of Inquiry on Post Election Violence, only 98 of the 1,133 conflict deaths occurred in Western Province (Waki, 2008). The majority of conflict deaths in Western Province occurred in districts that bordered Rift Valley Province; only 9 deaths were documented in Busia District (Waki, 2008). In addition, most KLPS2 respondents (95.4%) are members of the Luhya ethnic group, the majority ethnic group in Western Province; as such, they were somewhat less likely to be singled out as clearly aligned with either the incumbent, Mwai Kibaki (a member of a different ethnic group), or the opposition candidate, Raila Odinga (a member of a third group).10 Thus, though KLPS2 survey respondents lived through the crisis, both their physical locations and their ethnic identities helped to shield most of them from the worst of the violence.

This is not to say that KLPS2 respondents were safely removed from the fighting. The second wave of the survey included questions on exposure to violence during the postelection crisis. It documents the fact that relatively few respondents were themselves the victims of physical attacks, largely because they were able to hide in their homes during clashes.11 Of the KLPS2 wave 2 respondents, 71.7% said that they were “very worried” about their own safety and the safety of their family members during the crisis, and an additional 22.6% indicated that they were “somewhat worried.” In addition, 76.3% said that the crisis prevented them from going to local markets to obtain basic necessities. However, only 5.2% indicated that someone in their household was physically assaulted during the crisis. An additional 3.7% of respondents had property stolen or burned, but did not have a household member assaulted. Thus, KLPS2 respondents experienced the crisis firsthand, but relatively few were themselves victims of violence. Our estimates should therefore be seen as both a lower bound on the impact of civil conflict on risk preferences and a natural complement to studies that estimate the marginal impact of greater exposure to violence.

## III.  Measuring Risk Preferences

We elicit risk preferences by confronting survey respondents with a series of hypothetical decision problems. Our approach builds on the seminal work of Binswanger (1980) and more recent contributions by Barr and Genicot (2008) and Harrison, Humphrey, and Verschoor (2010). We focus on simple lottery structures and limited choice sets. Each of our decision problems was a choice between two or three lotteries involving two equally likely potential payoffs. The sequence of decision problems was designed to start with choices that were extremely simple, building slowly toward more complicated choice problems. This sequencing from least to most complex served two purposes. First, the gradual increase in complexity was intended to help address the concern that respondents might not exert sufficient cognitive effort (e.g., to calculate expected payoffs) when facing nonincentivized choice problems.12 Respondents first considered options that could be evaluated with minimal cognitive effort, easing into the process of evaluating the expected utility of financial lotteries. Second, we wished to maximize comprehension by subjects with low levels of numeracy (since many of our respondents had relatively little formal education). For this reason, we also limited each decision problem to a maximum of three lottery options, included only three easily understood probabilities (0, 0.5, and 1), and considered only lotteries over financial gains (rather than losses). Our experimental instructions do not assume any familiarity with probabilities, averages, or expected values; lotteries are explained in terms of payoffs and uncertain but equally likely events.13

When administering our experiment, survey enumerators began by presenting two practice decision problems that introduced the structure of the lottery choice questions to the respondent. The first practice problem contained only degenerate lotteries: the respondent was asked to choose between 100 and 150 Kenyan shillings.14 The second practice problem introduced the (nondegenerate) lottery concept in a setting with a clear “correct” answer: one lottery first-order stochastically dominated the other, and both involved risk. Enumerators asked respondents to choose between the lotteries presented in the practice decision problems, and then followed a script that made sure that all respondents fully understood the nature of the choices they were facing.

After completing the practice decision problems, each subject made six choices between lotteries that differed in riskiness. Each choice was presented on a laminated card depicting either two or three options. Like the practice problems, the first question (described above) provided a test of monotonicity, allowing us to identify subjects who were either not expected utility maximizers (Kőszegi & Rabin, 2006) or simply could not grasp the nature of the choice problems. The second decision problem offered an extremely simple test of risk preferences, and one that almost all subjects should have easily understood. Subjects were asked whether they preferred to receive 100 shillings with certainty, or a lottery that paid 0 and 400 shillings with equal probability. The remaining four decision problems presented lottery choices of increasing complexity. Without any functional form assumptions (but assuming subjects were maximizing a well-defined utility function), these decisions can be used to classify subjects into risk preference categories: risk loving, risk neutral, moderately risk averse, and most risk averse (always choosing the lotteries with the lowest expected value and payoff spread). If we assume that consistent preferences can be represented by a utility function of the constant relative risk aversion (CRRA) form, the risk cards were calibrated to distinguish a wide range of coefficients.15 A subject with a CRRA coefficient of 1.78 or higher would always choose the lowest-variance, lowest-expected-value lottery, while a subject with a CRRA coefficient of 0.19 or less would always choose the lottery with the highest expected value (or, if she were risk loving, the highest variance). The payouts for the lotteries in all the choice problems included in our experiment are described in online appendix table A1.

### A.  Individual Choices

Histograms of individual choices in all six decision problems are presented in online appendix figure A1. Very few respondents (only 4.14%) indicated that they preferred the degenerate lottery, which paid 100 Kenyan shillings with certainty, to a nondegenerate lottery, which paid either 100 or 120 Kenyan shillings, each with probability 0.5. We interpret this as evidence that most subjects understood the nature of the decision problems, at least those that involved relatively simple payoff calculations.16

Using data from the other five decision problems allows us to assign respondents to distinct risk preference categories and to test whether individual decisions are consistent with a CRRA utility representation. There are 162 possible combinations of responses to the last 5 lottery choice problems, only 10 of which are consistent with CRRA utility. We found that 22.5% of respondents always chose the lowest variance, lowest expected value lottery. This choice pattern is consistent with a CRRA coefficient of 1.78 or above. While 2.4% of respondents always chose the highest expected value lottery, 15.7% always chose the highest variance lottery (the highest variance lottery is the highest expected value lottery in four of the five decision problems). A risk-loving individual with a CRRA coefficient below $-0.26$ would always choose the highest variance lottery, while an individual with a CRRA coefficient between $-0.26$ and 0.19 would always choose the lottery with the highest expected value. Among the respondents, 4.0% made decisions that were consistent with a CRRA coefficient between 0.19 and 1.78, indicating an intermediate degree of risk aversion. Thus, 44.6% of respondents made choices consistent with the maximization of a CRRA utility function, but almost all of these individuals were at the extremes—consistently choosing either the lowest or the highest variance lotteries offered.

This choice patterns suggest that a CRRA coefficient is not the best way to summarize our respondents' risk preferences. Instead, we construct a simple index of risk tolerance: a count of the number of times (out of five lottery choice questions) that a subject chose the highest variance or highest expected value lottery. This index has two important strengths. First, it obviates the need to impose functional form assumptions on the structure of risk preferences. In the decision problems included in our study, all lotteries involving risk have two equally likely outcomes. In four of the five decision problems, the highest expected value lottery has the highest variance and the lowest minimum payoff (i.e., the lowest payoff in the bad state).17 Hence, any parametric restriction that permits an ordering of utility functions in terms of risk aversion would predict that relatively more risk-averse individuals would be less likely to choose the higher variance lotteries. Second, constructing a measure of risk aversion that does not rely on functional form assumptions allows us to use data from all subjects, including those whose choices were not perfectly consistent with a specific utility representation. As discussed in Loomes (2005) and Choi et al. (2014), most subjects implement their choices with error, and we would expect relatively high levels of error in our sample because of the relatively low level of formal schooling attained by our subjects.18 Using a simple index of risk tolerance that can be calculated for all subjects allows us to maximize statistical power by using all of our data and eliminates the possibility that selection into the pool of CRRA-consistent subjects might drive our results.

### B.  Instrument Validity

To address concerns about the validity of hypothetical measures of risk aversion, we test whether individual responses to our hypothetical lottery choice questions explain observed variation in behaviors that we might expect to be driven (at least in part) by risk attitudes. We focus on two such behaviors suggested by the literature: entrepreneurship (Schumpeter, 1934; Skriabikova, Dohmen, & Kriechel, 2014) and migration in search of employment (Jaeger et al., 2010, Bryan, Chowdhury, & Mobarak, 2014).19 Both of these actions can be seen through the lens of risk tolerance: for an unemployed or underemployed young adult residing in a rural area, operating one's own business and migrating are two high-risk but potentially profitable strategies for improving one's long-term income prospects. Both behaviors are also relatively uncommon in our sample: only 12.4% of KLPS2 respondents were operating their own business at the time of the survey, and only 3.5% had ever moved for a job or in search of work. To increase power, we also consider an aggregate index of risk taking equal to 1 if a respondent is either self-employed or has ever migrated for work.

We document the association between these risky but potentially profitable activities and responses to our lottery choice questions in online appendix table A3. The number of times a respondent opted for the riskiest lottery is significantly associated with the likelihood of operating one's own business, migrating for work, and our aggregate index that combines the two behaviors. We show in online appendix table A4 that the same relationships generally hold within the precrisis and postcrisis periods. Given the many factors underlying occupational choices, we interpret these robust associations as evidence that our lottery choice measure predicts outcomes associated with risk aversion in the cross-section.

## IV.  Analysis

### A.  Identification Strategies

We exploit the fact that Kenya's postelection crisis occurred in the middle of the KLPS2 data collection effort to estimate the impact of the violence on risk preferences. The KLPS2 survey was launched in August 2007, and 1,179 respondents were surveyed in 2007 prior to the elections. The crisis led to a two-month suspension of survey activities, which resumed in March 2008 and continued through the end of 2009. We employ two complementary identification strategies. First, we estimate the impact of the crisis in a straightforward linear framework. We report specifications that include calendar month fixed effects, enumerator fixed effects, and controls for sociodemographic characteristics such as respondent age, educational attainment, and marital status that we expect to change gradually over time as respondents transition to adulthood.20 Thus, we estimate OLS regressions of the form
$Yijm=α+βPosti+δXi+ηj+λm+ɛijm,$
(1)
where $Yijm$ denotes the risk aversion index of respondent $i$ surveyed by enumerator $j$ in month $m$, $Posti$ is an indicator variable equal to 1 if respondent $i$ was surveyed after the postelection crisis, $ηj$ is an enumerator fixed effect, $λm$ is a calendar-month fixed effect, and $ɛijm$ is a conditionally mean-zero error term.21In the online appendix, we also present two alternative specifications as robustness checks: ordered logit specifications that account for the ordered nature of our outcome variable and OLS specifications that replace the month fixed effects with separate linear time trends for the precrisis and postcrisis periods.22
We also report complementary instrumental variables' estimates of the impact of the postelection crisis on individual risk preferences, exploiting the fact that KLPS2 respondents were randomly assigned to one of two waves of surveying. Wave 1 began in August 2007 and continued through November 2008, while wave 2 started in November 2008 and concluded in December 2009. As discussed above, Kenya's postelection crisis occurred approximately halfway through the first wave of surveys: 1,179 wave 1 surveys were completed before the crisis, and 1,289 were completed afterward. This enables us to use random assignment to wave 2 as an instrument for being surveyed after the crisis. Within each wave, participant characteristics may be associated with how quickly an individual was surveyed, for example, subjects who were still residing with their parents in their home villages might have been surveyed earlier because they were easier to locate. However, random assignment to survey wave creates exogenous variation in exposure to civil conflict prior to the survey. Thus, our 2SLS regressions are of the form
$Yijm=α1+β1Posti+δ1Xi+η1j+λ1m+ζ1ijm,$
(2)
$Posti=α2+γ2Wave2i+δ2Xi+η2j+λ2m+ζ2ijm,$
(3)
where all variables are as before, $β1$ is the coefficient of interest, $Wave2i$ is an indicator equal to 1 for those randomly assigned to the second wave of surveying, and both $ζ1ijm$ and $ζ2ijm$ are conditionally mean-zero error terms. The variable $Wave2i$ takes the value 1 for individuals assigned to be surveyed in wave 2 (which is entirely postcrisis) and 0 for those assigned to be surveyed in wave 1 (which includes both pre- and postcrisis observations).23

### B.  Results

We begin with a graphical presentation of our key result. Figure 1 plots the average of our risk index—the number of times a respondent chose the highest variance or highest expected value lottery—as a function of the month and year in which the survey was administered. The figure highlights the marked drop in the tendency to choose risky lotteries after the crisis. Prior to the crisis, the median value of the risk index was 3; it dropped to 1 after the crisis. For a subject whose choices can be represented by a CRRA utility function, a risk index of 3 indicates a CRRA coefficient between 0.46 and 0.50, while a risk index of 1 indicates a CRRA coefficient of at least 0.72.24 Thus, the onset of the crisis is associated with a substantial increase in risk aversion.

Figure 1.

Risk Preferences before and after Kenya's Postelection Crisis

Figure 1.

Risk Preferences before and after Kenya's Postelection Crisis

Figure 2 presents histograms of our risk index separately for the precrisis and postcrisis periods. The figure shows that 0 risky choices was the modal outcome after the crisis. Respondents were more likely to choose the riskiest lottery zero or one times after the crisis, and they were less likely to choose the riskiest lottery two, three, four, or five times after the crisis. Moreover, all of these differences are statistically significant.25

Figure 2.

Histogram of Primary Risk Index before and after the Postelection Crisis

Figure 2.

Histogram of Primary Risk Index before and after the Postelection Crisis

#### OLS results.

We now proceed to estimate the impact of exposure to the postelection crisis on risk preferences by estimating equation (1). Our dependent variable is the number of times a respondent chose the highest variance or highest expected value lottery (over the course of five decision problems). Results are reported in table 1. In column 1, we include only the indicator for being surveyed after the postelection crisis. In column 2, we control for gender, age, education level, and marital status at the time of the survey. In column 3, we control for survey enumerator fixed effects. In column 4, we control for the month of the year in which the survey took place (to eliminate any seasonal patterns in responses). We include all three sets of controls in column 5.

Table 1.
OLS Regressions of the Impact of the Postelection Crisis on Risk Preferences
Specification:OLS (1)OLS (2)OLS (3)OLS (4)OLS (5)
Surveyed after −0.682*** −0.685*** −0.798*** −0.559*** −0.734***
postelection crisis (0.117) (0.114) (0.118) (0.085) (0.088)
Demographic controls No Yes No No Yes
Interviewer controls No No Yes No Yes
Month controls No No No Yes Yes
Observations 5,047 5,047 5,047 5,047 5,047
$R2$ 0.023 0.028 0.151 0.027 0.157
Specification:OLS (1)OLS (2)OLS (3)OLS (4)OLS (5)
Surveyed after −0.682*** −0.685*** −0.798*** −0.559*** −0.734***
postelection crisis (0.117) (0.114) (0.118) (0.085) (0.088)
Demographic controls No Yes No No Yes
Interviewer controls No No Yes No Yes
Month controls No No No Yes Yes
Observations 5,047 5,047 5,047 5,047 5,047
$R2$ 0.023 0.028 0.151 0.027 0.157

Robust standard errors clustered at the month level in all specifications. Outcome variable is the number of times a respondent chose the riskiest (i.e., highest variance or highest expected value) lottery (out of five). Columns 2 and 5 include controls for gender, age, education level, and marital status (at the time of the survey). Significant at $***$1%, $**$5%, and $*$10%.

In all five OLS specifications reported in table 1, the postelection coefficient is negative and significant at least at the 99% confidence level, suggesting that experiencing the crisis lowered the number of risky choices a respondent made by between 0.559 and 0.798 choices.26 In the precrisis period, the average number of risky choices was 2.564 out of five, so the change observed after the crisis represents a dramatic drop in the willingness to bear profitable risk. Adding controls for gender, education level, age, and marital status has almost no impact on the estimated coefficient.27

We consider alternative formulations of the outcome variable in table 2. In the first column, the outcome variable is an indicator for always choosing the highest variance or highest expected value lottery option (i.e., behaving in a manner consistent with risk-neutral or risk-loving preferences—specifically, a CRRA coefficient no greater than 0.19). In the second column, the outcome is an indicator for always choosing the lowest variance, lowest expected value alternative (i.e., behaving in a manner consistent with a CRRA coefficient of at least 1.78). We find that the postelection crisis led to a 5.6 percentage point (26.1%) decrease in the likelihood of making risk-neutral or risk-loving choices and a 10.9 percentage point (81.7%) increase in the probability of always choosing the lowest variance, lowest expected return lottery. We then consider each decision problem in isolation. The postelection crisis led to a significant decrease in the likelihood of choosing higher variance, higher expected value lottery options in each of the five decision problems.28 Thus, our main result is robust to a wide range of alternative specifications and formulations of the outcome variable.

Table 2.
OLS Regressions of the Impact of the Postelection Crisis on Alternate Measures of Risk Aversion
Choice on Decision Number
Dependent Variable:Risk Neutral or LovingMost Risk Averse23456
Specification:OLS (1)OLS (2)OLS (3)OLS (4)OLS (5)OLS (6)OLS (7)
Surveyed after postelection crisis −0.056*** 0.109*** −0.114*** −0.233*** −0.296*** −0.290*** −0.260***
(0.017) (0.023) (0.027) (0.045) (0.061) (0.031) (0.053)
Observations 5,047 5,047 5,047 5,047 5,047 5,047 5,047
$R2$ 0.007 0.033 0.015 0.017 0.027 0.023 0.025
Choice on Decision Number
Dependent Variable:Risk Neutral or LovingMost Risk Averse23456
Specification:OLS (1)OLS (2)OLS (3)OLS (4)OLS (5)OLS (6)OLS (7)
Surveyed after postelection crisis −0.056*** 0.109*** −0.114*** −0.233*** −0.296*** −0.290*** −0.260***
(0.017) (0.023) (0.027) (0.045) (0.061) (0.031) (0.053)
Observations 5,047 5,047 5,047 5,047 5,047 5,047 5,047
$R2$ 0.007 0.033 0.015 0.017 0.027 0.023 0.025

Robust standard errors clustered at the month level in all specifications. All specifications include controls for gender, age, education level, and marital status (at the time of the survey). Thus, the specifications in this table mirror those in table 1, column 2. Here, the outcome variables vary by column. The outcome in column 1 is an indicator for making choices that can be rationalized by a CRRA coefficient of 0.19 or less (i.e., always choosing the highest variance or highest expected value lottery). In column 2, the outcome variable is an indicator for behaving in a manner consistent with a CRRA coefficient of 1.78 or above (always choosing the lowest variance, lowest expected value lottery), so its sign is opposite those in other columns and tables. Columns 3 through 7 use discrete representations of the separate decision problems as outcomes, ordered by risk aversion; thus, the dependent variable in column 3 is an indicator for choosing the higher variance lottery in decision problem 2. The dependent variables in the remaining columns take on the values 1, 2, and 3, with 1 being the least risky (i.e., lowest variance, lowest expected value) lottery and 3 being the riskiest (i.e., highest variance, highest expected value) lottery. Significant at $***$1%, $**$5%, and $*$10%.

#### Results.

Next, we employ a complementary identification strategy, exploiting the fact that KLPS2 respondents were randomly assigned to one of two waves of surveying to generate instrumental variables estimates of the impact of the postelection violence on measured risk aversion. Two-stage least squares (2SLS) regression results are reported in table 3. In panel A, the outcome variable is the number of times that a respondent chose the highest variance, highest expected value lottery alternative. In column 1, we report estimates from a parsimonious specification that includes no covariates. Coefficient estimates indicate that the postelection crisis had a large and statistically significant impact on measured risk preferences, reducing the number of times (out of five) that respondents opted for the riskiest, highest expected value lottery by approximately one full decision problem. Again, relative to a mean number of risky choices of 2.564 in the precrisis period, this is an extremely large effect. In columns 2 through 5, we include controls for individual demographic characteristics (gender, age, education level, and marital status), the identity of the survey enumerator, and the calendar month in which the interview took place. Coefficient estimates are consistently negative and significant. Thus, our 2SLS estimates are consistent with our OLS results: Kenya's postelection crisis appears to have made survey respondents substantially more risk averse.

Table 3.
IV Regressions of the Impact of the Postelection Crisis on Risk Preferences
2SLS2SLS2SLS2SLS
Specification:2SLS (1)2SLS (2)2SLS (3)2SLS (4)2SLS (5)
A. Dependent variable: Number of risky (highest variance) choices (out of 5)
Surveyed after postelection crisis −0.986*** −1.050*** −1.670*** −1.010*** −1.994***
(0.202) (0.224) (0.443) (0.229) (0.59)
B. Dependent variable: Choices consistent with being risk neutral or risk loving
Surveyed after postelection crisis −0.065** −0.083** −0.067* −0.080*** −0.119**
(0.029) (0.034) (0.035) (0.031) (0.053)
C. Dependent variable: Choices consistent with being most risk averse
Surveyed after postelection crisis 0.212*** 0.212*** 0.322*** 0.223*** 0.349***
(0.063) (0.065) (0.117) (0.071) (0.119)
First-stage $F$-statistic 9.66 9.23 8.54 14.38 11.54
Demographic controls No Yes No No Yes
Interviewer controls No No Yes No Yes
Month controls No No No Yes Yes
Observations 5,047 5,047 5,047 5,047 5,047
2SLS2SLS2SLS2SLS
Specification:2SLS (1)2SLS (2)2SLS (3)2SLS (4)2SLS (5)
A. Dependent variable: Number of risky (highest variance) choices (out of 5)
Surveyed after postelection crisis −0.986*** −1.050*** −1.670*** −1.010*** −1.994***
(0.202) (0.224) (0.443) (0.229) (0.59)
B. Dependent variable: Choices consistent with being risk neutral or risk loving
Surveyed after postelection crisis −0.065** −0.083** −0.067* −0.080*** −0.119**
(0.029) (0.034) (0.035) (0.031) (0.053)
C. Dependent variable: Choices consistent with being most risk averse
Surveyed after postelection crisis 0.212*** 0.212*** 0.322*** 0.223*** 0.349***
(0.063) (0.065) (0.117) (0.071) (0.119)
First-stage $F$-statistic 9.66 9.23 8.54 14.38 11.54
Demographic controls No Yes No No Yes
Interviewer controls No No Yes No Yes
Month controls No No No Yes Yes
Observations 5,047 5,047 5,047 5,047 5,047

Robust standard errors clustered by survey month. All specifications include controls for gender, age, education level, and marital status. We instrument for being surveyed after the postelection crisis with the indicator for being randomly assigned to the second wave of surveying. The outcome variables are: in panel A, the number of times a respondent chose the riskiest lottery (out of five); in panel B, an indicator for making risk-neutral or risk-loving choices; in panel C, an indicator for always choosing the lowest variance, lowest expected-value lottery.

In panels B and C of table 3, we consider two alternative formulations of our dependent variable. In panel B, we estimate the impact of the postelection crisis on the likelihood of making choices consistent with risk-neutral or risk-loving preferences (by always choosing the highest variance or highest expected value lottery). Coefficient estimates suggest that exposure to the postelection violence decreased the likelihood of being risk neutral or risk loving by between 6.5 and 11.9 percentage points. In panel C of table 3, we present 2SLS estimates of the impact of the crisis on the likelihood of always choosing the lowest variance lottery. Coefficient estimates suggest that the crisis increased the likelihood of extreme risk aversion (consistent with a CRRA coefficient in excess of 1.78) by between 21.2 and 34.9 percentage points. In the precrisis period, only 13.4% of respondents displayed this level of risk aversion. Thus, 2SLS estimates suggest that the postelection violence more than doubled the likelihood of being extremely risk averse.

### C.  Threats to Identification

Thus far, we have shown that two distinct identification strategies generate similar estimates of the impact of Kenya's postelection violence on individual risk preferences. An important caveat is that both identification strategies exploit the timing of the crisis, so any other major shock that coincided with the postelection crisis could be driving our results. As is often the case, Kenya's episode of civil conflict created increased uncertainty about the country's economic and political future (though it did not, in the end, lead to a change in the head of state). As discussed above, such macroeconomic and political uncertainty is typical of civil strife, and a strength of our estimation strategy is that we capture the overall impacts of conflict on society—but this also means that we cannot, for example, separate the impacts of fear of violence from the impacts of political uncertainty. Nonetheless, to the extent possible, it is important to rule out the possibility that shocks coincident with, but not related to, the postelection crisis could explain our results.

One obvious concern is that the crisis might have triggered a period of high inflation and that our results are driven by price changes rather than the conflict itself. Inflation rates were relatively high during and after the crisis: the CPI increased by more than 2% in January, April, and May 2008.29 It is likely that these high rates of inflation were at least partly attributable to the crisis itself (though Kenya experienced many other months of high inflation in the years before and after the crisis) and should therefore be viewed as a potential mediating factor rather than a competing explanation of our findings. We test whether inflation alone could explain our empirical results by replicating our main OLS and 2SLS specifications controlling for the inflation rate (results reported in online appendix tables A8 through A11). All of our results are robust to including the inflation rate as a covariate; we find no evidence that the observed impact of conflict is explained by (only) the price instability created by the crisis.30

Another possible concern, already discussed, is that our results could be driven by the fact that respondents surveyed after the postelection violence were, on average, older when they were surveyed: the surveys were conducted over a two-year period, and we compare those surveyed before the violence to those surveyed afterward. We attempt to address this issue by directly controlling for age and other factors (e.g., marital status and educational level) likely to change gradually over time as respondents grow up. However, if risk preferences change discretely at some point during the transition to adulthood, it is possible that a critical mass of respondents “aged out” of their youthful, risk-tolerant period around the time of the crisis. Fortunately, our data allow for a clear test of this hypothesis, since the sample includes a broad range of birth years. In online appendix figure A4, we plot the average number of risky lottery choices (out of five) among respondents at each age level, separated by whether the survey took place before or after the postelection crisis. The figure shows that there is no discrete drop in risk tolerance at any particular age; instead, risk aversion appears relatively constant across the age range included in our sample. However, at all age levels, we see lower levels of risk tolerance after the crisis. Thus, our results do not appear to be driven by the fact that those surveyed after the postelection violence were, on average, older at the time that they were surveyed.

### D.  Other Impacts of the Postelection Crisis

We interpret our results as evidence that civil conflict has impacts on individual risk preferences. An important question is what, if any, mechanism or mechanisms explain these impacts. One possibility is that the postelection violence was an economic shock and that young adults expected it to slow growth and reduce job opportunities. If having a lower expected permanent income makes one less willing to bear risk, such a shock might have changed risk tolerance through job prospects.

To test this hypothesis, we estimate the impact of the postelection crisis on income-generating activities and wages directly. Results are reported in online appendix table A12. We find no evidence that the postelection crisis reduced employment opportunities or income. The crisis did not have a significant impact on either the likelihood of reporting any income-generating activity (i.e., either employment or self-employment) or wages conditional on employment. It appears to have weakly increased the likelihood of being employed, but weakly decreased the likelihood of self-employment. None of these impacts is significant across the full range of specifications. Though many respondents were unable to work during the crisis, any negative impacts on respondents' wages and income seem to have disappeared after the crisis ended.31

Interestingly, however, we find strong evidence that respondents believed that the postelection violence lowered incomes. The KLPS2 survey asked respondents to report their beliefs about average monthly incomes in both Busia (the rural home area of KLPS2 respondents) and Nairobi. Importantly, these questions ask about current monthly income, so they should not reflect the very short-term impacts of being unable to work during the crisis. Results (reported on online appendix table A12) indicate that the postelection crisis led to a dramatic decline in perceived income levels. Coefficient estimates suggest that the crisis caused more than a 25% decline in perceived average incomes; the effect is significant across a range of specifications.32 Thus, young people believed that the postelection crisis was a negative income shock, but we find no evidence that for these respondents, it actually was one.33

The postelection violence also appears to have changed the way KLPS2 respondents evaluate different job opportunities. The survey asks respondents to indicate which of six job attributes are the most important when they search for employment. The results (again reported on online appendix table A12) show that the postelection crisis increased the likelihood of prioritizing job security (specifically, finding “a safe job, with no risk of closing down or unemployment”) by at least 13.9 percentage points—as we would expect if the crisis increased risk aversion. The crisis also decreased the likelihood of prioritizing a job that put one close to “friends and relatives.” Interestingly, the crisis does not appear to have affected the likelihood of wanting a job that allowed one to work for or with members of one's own ethnic group.

We do, however, find substantial evidence that the postelection crisis changed the social fabric of the country, even in areas like Busia District that were less affected than other parts of Kenya. The crisis destroyed social capital. We find a consistently significant negative impact of the crisis on the likelihood of being involved in at least one community group (online appendix table A12). The postelection crisis also had a dramatic impact on generalized trust, cutting the number of respondents who believe most people can be trusted by more than 50%. In addition, the crisis had a consistently significant negative impact on the extent to which respondents trust members of other ethnic groups; point estimates suggest that trust in one's own ethnic group also declined, but the effect is not consistently significant. Though the overwhelming majority of KLPS2 respondents are from the Luhya ethnic group, so neither the president nor the main opposition candidate was a member of his ethnic group, this decline in trust across ethnic lines is consistent with the general pattern of postelection violence.34

Thus, though the crisis does not appear to have affected the incomes and job market prospects of KLPS2 respondents, we find suggestive evidence that respondents believed that it did. It is clear that they believed that average incomes were lower after the violence, and they also shifted toward prioritizing job security over other job attributes. Yet those respondents least likely to be engaged in the labor market experienced larger impacts: their preference changes were larger. At the same time, we also find that the crisis eroded trust and destroyed social capital. Of course, violence may change many aspects of society, and it is impossible to fully distinguish between mechanisms (driving the change in risk preferences) and other outcomes (that were simultaneously affected by the postelection violence). Moreover, as others have noted, the willingness to trust and the willingness to take risks are, from a theoretical perspective, closely related (Karlan, 2005; Schechter, 2007), so in fact, both the observed shift toward prioritizing job security and the observed decline in trust may be partially attributable to the observed increase in risk aversion. Importantly, however, the evidence suggests that the postelection violence did not affect risk preferences primarily through a labor market channel (i.e., through a dramatic drop in income); instead, we find suggestive evidence that the violence had a direct impact on individual preferences, beliefs, and values.

## V.  Conclusion

We measure the impact of Kenya's postelection violence on individual risk preferences. We find that experiencing the postelection crisis appears to have increased risk aversion significantly. Point estimates suggest that exposure to the crisis decreased the likelihood of making risk-neutral or risk-loving choices by 5.6 percentage points (26.1%) and increased the likelihood of always choosing the lowest variance, lowest expected value lottery by 10.9 percentage points (81.7%). Our results are robust to a range of controls and the use of entirely distinct identification strategies. Thus, the evidence suggests that exposure to the postelection crisis led to a statistically and economically significant decrease in the willingness to take profitable risks.

In relation to existing studies of the determinants of individual preferences, our results corroborate a growing body of evidence that preferences are affected by major life events such as conflicts, disasters, and economic downturns. Identification of the impacts of such major events is always challenging since exogenous variation in exposure to historical shocks is rare. Studies of the impact of conflict on individual preferences have estimated the marginal impact of greater exposure to violence, implicitly treating less-exposed survivors as a comparison group. We are able to expand this literature because our identification strategies enable us to measure the effect of civil conflict on a broad population, using respondents who had not (yet) lived through the crisis as our comparison group. Relatively more conflict-affected individuals may become more pro-social or less risk averse (Bauer et al., 2014; Callen et al., 2014), but the impact on the population as a whole is a shift toward less willingness to take profitable risks. We estimate the combined effects of violence and any attendant change in perceptions of political uncertainty. The drawback to this approach is that we cannot separate the effect of violence from the effects of concomitant changes in Kenya's political situation. However, this combination of violence and political uncertainty is inherent in almost all civil conflicts: the relevant estimand is, in fact, their combined effect.

Though both the political crisis and the economic downturn triggered by the postelection crisis were relatively short-lived, we find that the impacts on risk preferences persisted for more than a year. Moreover, our results suggest that the channel of impact is not (primarily) economic since the probability of engaging in any income-generating activity is not affected by the violence, but generalized trust and social capital are. Our results therefore suggest that conflict may have long-lasting impacts on economic development through channels such as reduced entrepreneurship. That our findings differ from some earlier studies suggests that the impacts of conflict at the scale of affected individuals and villages may not generalize to the scale of a district or that of a nation.

## Notes

1

See the review article by Bauer et al. (2016) for discussion.

2

This description of Kenya's 2007–2008 postelection crisis draws on several sources: McCrummen (2007), BBC (2008a, 2008b), Waki (2008), World Bank (2008, 2010), and Van Praag (2010).

3

The lottery choice questions are described in table A1 in the online appendix.

4

Importantly, the comparison groups in Voors et al. (2012) and Callen et al. (2014) are made up of individuals who lived through a civil conflict but were (individually or on average) less exposed to violence than individuals in the treatment groups. For example, Callen et al. (2014) define treatment at the neighborhood level, based on the polling station closest to a respondent's residence; if an attack occurred within 1 kilometer of a polling station and that polling station was the one closest to the attack, the neighborhood is defined as treated (in their main analysis, though, they provide a series of robustness checks employing alternative definitions of treatment). So neighborhoods that were closest to successful attacks are treated, while those that were farther from successful attacks make up the comparison group. However, even the comparison group was exposed to violence, though they were, in expectation, less exposed to violence than the treatment group. Indeed, 89.9% of the polling stations in their sample were within 3 kilometers of a successful attack, so any estimate of the impact of that (lower) level of exposure would be extremely imprecise. Similar identification strategies are used in Bellows and Miguel (2009), Voors et al. (2012), and Bauer et al. (2014). What differentiates our identification strategy from these is that our comparison group comprises individuals who had not (yet) experienced the period of violence that we study.

5

It is important to note that the population we study is not representative of Kenya as a whole. It is, however, broadly representative of the population of young people from one particular region and thus provides a window into the impacts of conflict on society. As we discuss further below, our data come from a follow-up survey of a health intervention that was implemented in all the public primary schools in a specific rural district; as such, the population is broadly representative of the sample of individuals enrolled in government schools in that area at the time of the intervention.

6

Related work by Campos-Vazquez and Cuilty (2014) corroborates this finding by showing that priming Mexican students with information about drug violence increases risk aversion.

7

In the domain of time preferences, Meier and Sprenger (2012) show that experimental measures of patience predict creditworthiness. Fisman, Jakiela, and Kariv (2017) show that experimental measures of equality-efficiency trade-offs predict voting behavior, while Fisman et al. (2015) show that the same measure predicts the postgraduation career choices of law students.

8

See Ashraf, Karlan, and Yin (2006) for a notable exception.

9

KLPS2 was a long-term follow-up of the Primary School Deworming Project (PSDP) that was implemented in Busia District in Kenya's Western Province between 1998 and 2001. All KLPS2 respondents were enrolled in public primary schools in the project area in 1998. See Miguel and Kremer (2004) for discussion of the PSDP.

10

Western Province was an opposition stronghold, and Raila Odinga received 64.6% of the votes cast there in the presidential election; thus, individuals perceived as likely supporters of the incumbent were the most at risk. We thank the World Bank's Kenya Country Office for guidance on wording.

11

KLPS2 respondents were randomly assigned to one of two waves of surveying. The postelection violence interrupted the first wave of surveying. Questions about exposure to postelection violence were included only in wave 2, so responses can be seen as representative of the entire respondent population. These additional questions were included near the end of the survey, after the risk preference elicitation questions, so their inclusion could not have affected measured risk preferences directly by priming respondents. See Callen et al. (2014) for a discussion of the impact of fearful recollections on measured risk preferences.

12

There is some debate about the extent to which nonincentivized lottery choice questions correctly measure individual risk preferences. See Camerer (1995) for an overview and Binswanger (1980) and Holt and Laury (2002) for seminal contributions. Evidence suggests that financial incentives induce greater risk aversion (Camerer & Hogarth, 1999). Embedding nonincentivized decision problems in surveys has nonetheless proven successful in a number of field settings in developing countries when conducting incentivized experiments at scale is not feasible (Ashraf et al., 2006; Callen et al., 2014).

13

Complete experimental instructions are included in the online appendix.

14

The average U.S. dollar value of 100 Kenyan shillings was 1.36 over the period during which the KLPS2 survey was in the field, from August 2007 to December 2009. During that period, 150 to 200 shillings was a typical daily wage for informal agricultural labor.

15

The CRRA utility function takes the form $u(x)=x1-ρ/(1-ρ)$ where $ρ$ indicates the level of risk aversion. Higher values of $ρ$ indicate greater risk aversion. When $ρ$ equals 0, the agent is risk neutral; the indifference curves represented by the CRRA utility function approach log utility as $ρ$ approaches 1. Even if relative risk aversion is not constant, constant relative risk aversion is a reasonable approximation over the relatively small range of payoffs considered in our experiment.

16

We also asked enumerators to indicate whether they believed that respondents fully understood the lottery choice questions. The responses suggest that 99.6% of subjects fully comprehended the choices they were making. There are, of course, several reasons that subjects who understood the decision problem might prefer a degenerate lottery to a stochastically dominant one involving risk. One possibility is that some respondents have preferences that are not monotonic. Several nonexpected utility models of risk preferences suggest that individuals may prefer to avoid increases in payoff variance, even when the higher variance lottery stochastically dominates the lower variance alternative (Kahneman & Tversky, 1979; Kőszegi & Rabin, 2006). We interpret the overwhelming tendency to choose the stochastically dominant lottery as evidence against strongly nonmonotonic preferences. One plausible interpretation of the observed choice patterns is that respondents have monotonic preferences that they implement with error (Hey & Orme, 1994; Loomes, 2005; Von Gaudecker, van Soest, & Wengström, 2011; Choi et al., 2014). Interestingly, subjects are much less likely to choose the dominated lottery after the postelection crisis; the percentage of respondents choosing the degenerate lottery drops from 11.0 before the crisis to 2.0 afterward.

17

The one exception is the final lottery choice question, which included an alternative designed to distinguish between risk-loving and risk-neutral types. In this choice problem, we classify both the highest expected value lottery and the highest variance lottery as risky when we construct our index of risk tolerance—so both risk-loving and risk-neutral types have risk tolerance indices equal to 5. Though coefficient magnitudes change somewhat, our substantive results are unchanged if we exclude the last decision problem from our index of risk tolerance or code the highest expected value lottery as a less risky choice in the final decision problem.

18

Respondents were 5.4 percentage points more likely to make choices consistent with a CRRA representation after the postelection crisis. If the likelihood of making consistent choices was also associated with risk aversion, omitting the inconsistent subjects could bias our results. However, all of our findings are robust to the exclusion of the inconsistent types from the analysis.

19

Though many studies in developed countries find a strong association between gender and risk aversion, the available evidence suggests that this pattern may be driven by high levels of risk tolerance among white men (Croson & Gneezy, 2009). It is therefore not appropriate to validate our results using gender. In fact, we do not find a strong association between gender and risk aversion: women are less likely to be risk loving but are also less likely to be extremely risk averse. The absence of a relationship between gender and risk aversion in rural Kenya is consistent with the findings reported in Jakiela and Ozier (2016).

20

Because the postelection violence occurred after only five months of surveying, any seasonal variation in risk preferences (e.g., variation across the crop cycle) could confound our estimates of the impact of the crisis; including calender-month fixed effects addresses this concern.With the exception of age, these characteristics might also be affected by the crisis. To address concerns about the potential for a bad controls problem, we also report specifications that omit all sociodemographic controls. Results are always similar in magnitude and significance with and without controls.

21

Since our identification is based on temporal variation in treatment status, we cluster our analysis at the month level. Results are similar in magnitude and significance if we cluster at the primary school (i.e., community) level, or if we include primary school fixed effects.As discussed above, our main outcome variable is the number of times a respondent chose the highest variance or highest expected value value lottery. In principle, it would be possible to use CRRA coefficients implied by an individual's choices as the outcome variable, but this would require us to exclude from the analysis the 55% of subjects whose choices were not consistent with a CRRA utility representation. All of our results are similar if we omit those subjects; however, because subjects are 5.4 percentage points more likely to make consistent choices after the postelection crisis, omitting inconsistent subjects could bias our findings.

22

While it is tempting to view our research design as analogous to a regression discontinuity approach, our natural experiment does not create a valid discontinuity. First, because the postelection crisis halted surveying for more than two months, sociodemographic characteristics such as age do jump discontinuously at the moment of the crisis. Second, because the crisis lasted months, the limit-based notion of regression discontinuity is not directly applicable to this setting; a discontinuity would involve choosing a single point in time during the crisis, and at any such point, data from this survey would not be immediately adjacent on both sides. Third, there is some evidence that neither the onset nor the conclusion of the crisis was in fact instantaneous and completely unexpected. Though opposition candidate Raila Odinga held a convincing lead in opinion polls several months before the election, incumbent Mwai Kibabki caught up with Odinga in the month prior to the polling date, potentially raising fears that one of the candidates might try to manipulate a close vote. The official report of the Commission of Inquiry also documents several minor clashes in Rift Valley in late November and early December, most of which appeared to be connected to attempts by political candidates to rally support by playing off of underlying ethnic tensions and disagreements over landownership (Waki, 2008). There was also a period of uncertainty in the wake of the crisis, between February 28, 2008, when the power-sharing agreement was signed, and April 12 when, after sometimes tense negotiations between the two political parties, Raila Odinga was sworn in as prime minister and the new coalition government officially took power.

23

Before proceeding to our 2SLS analysis, we check whether the random assignment of respondents to survey waves generated groups that were comparable in terms of observable characteristics prior to the survey. Because wave 2 respondents were surveyed approximately one year later than wave 1 respondents, we would not expect characteristics such as age at the time of the survey to be similar in the two waves. To test whether random assignment created groups that were comparable ex ante, it is necessary to focus on fixed traits and outcomes that were recorded in the survey for specific points in time. For example, the survey collects detailed information about school participation in each year between 1998 and the moment of the interview; this allows us to generate a variable indicating the number of years of schooling that a respondent had completed at the start of 2007 (before anyone was surveyed), regardless of the year in which a respondent was actually interviewed. Results are reported in online appendix table A2. We find no statistically significant differences between the survey waves in terms of proportion female, age in 2007, proportion born in Busia District, proportion from the local-majority Luhya ethnic group, years of schooling completed by 2007, and the proportion married by 2007. Thus, randomization appears to have succeeded in creating groups of respondents who were similar in terms of observable characteristics prior to the survey and the onset of the postelection violence.

24

Of course, as discussed above, most respondents in our sample implement their choices with error, so their preferences are not perfectly consistent with a CRRA utility representation.

25

Respondents were 16.9 percentage points more likely to have a risk index of 0 after the crisis ($p$-value $<0.001$), 2.3 percentage points more likely to have a risk index of 1 ($p$-value 0.075), 3.7 percentage points less likely to have a risk index of 2 ($p$-value 0.037), 3.4 percentage points less likely to have a risk index of 3 ($p$-value 0.014), 7.2 percentage points less likely to have a risk index of 4 ($p$-value $<0.001$), and 4.8 percentage points less likely to have a risk index of 5 ($p$-value 0.005).

26

Across the five specifications reported in table 1, the $p$-value on the indicator for being surveyed after the postelection crisis ranges from $1.082×10-8$ to $4.393×10-6$.

27

Controlling for enumerator fixed effects increases the estimated magnitude slightly, while controlling for calender month fixed effects leads to a small decrease in the estimated coefficient. We report a range of robustness checks in the online appendix. In online appendix table A5, we estimate ordered logit specifications that account for the discrete but ordered nature of the outcome variable. Again we find that the indicator for being surveyed after the postelection crisis is negative and significant in all specifications. In online appendix table A6, we include separate linear time trends for the precrisis and postcrisis periods. The indicator for being surveyed in the postcrisis period is negative and significant in all specifications.

28

The effect is similar in magnitude across the four decision problems that include three lottery alternatives rather than two. The estimated effect is also similar in magnitude in decisions problems that do and do not include a degenerate lottery that pays 100 Kenyan shillings with certainty. To further probe this issue, we examine the likelihood of choosing the safest (i.e., lowest variance, lowest return) lottery alternative in each of the five decision problems (results reported in online appendix table A7). We find no evidence that the shift toward lower-variance lotteries is larger in decision problems that included a degenerate lottery that did not involve uncertainty. Thus, our results contrast with those of Callen et al. (2014). They find a differentially larger impact of violence (specifically, of a psychological prime that induces recollection of fearful episodes) on risk tolerance when no risk-free alternative is available; their treatment appears to increase the preference for certainty in a way that “is at odds with both [expected utility] and cumulative prospect theory, but consistent with models that feature a specific preference for certainty” (Callen et al., 2014, p. 138). Our results are consistent with expected utility maximization, though they could also be explained by an increase in loss aversion in the model of reference dependence proposed by Kőszegi & Rabin (2006).

29

Online appendix figure A3 plots the monthly inflation rate (the percent change in prices relative to the previous month) from 2005 to 2010, using Consumer Price Index (CPI) data produced by the Kenya National Bureau of Statistics.

30

We also find no evidence of other aggregate shocks—for example, shocks to agricultural productivity—that could explain our results. Maize is the main staple crop for subsistence farmers in western Kenya, and sugarcane is the most widely grown cash crop. Data from the FAO statistical database indicate that Kenya's maize yield per hectare was slightly higher in 2007 than in the two previous years and overall production levels were comparable. Sugar yields and production levels in 2007 were also comparable to the previous five years. Thus, our results do not seem likely to be driven agricultural or other aggregate shocks that were not associated with the postelection crisis.

31

As a further test of the hypothesis that the postelection crisis affected risk tolerance because it affected individual earnings, we interact the indicator for being surveyed after the crisis with two characteristics likely to be associated with lower labor force attachment: educational attainment and gender. Intuitively, if negative wage impacts explain the effect of the crisis on risk tolerance, then we would expect smaller treatment effects in subpopulations that are less likely to be working outside the home. In online appendix table A13, we estimate the differential impact of the crisis on respondents who did not complete primary school (relative to those who did). To address the concern that the crisis might have affected the likelihood of completing primary school, we use an indicator for completing primary school by the end of 2006. Since most respondents were well above primary school age by 2006, the correlation between the indicators for completing primary school by the end of 2006 and completing primary school prior to the KLPS2 survey is quite high ($ρ$ = 0.91). These individuals are likely to engage in subsistence agriculture or work locally in low-skill occupations, making them less vulnerable to changes in urban labor markets where ethnic differences might be more important. We find that the crisis had a significantly larger negative impact on the risk tolerance of the less educated ($p$-value $<0.001$), though the impact is still significant among those who had completed primary school. When we examine treatment effect heterogeneity by gender—since women are less likely to participate in the labor market—coefficient estimates suggest that the crisis had a slightly larger impact on women than on men, though the effect is not statistically significant at conventional levels ($p$-value 0.103). Thus, we find no evidence that the crisis had a direct impact on wages or labor market opportunities, nor do we find evidence of a larger impact on those more likely to be involved in the formal labor market.

32

Incomes in the table are reported in 2007 U.S. dollars. Throughout the paper, incomes are deflated using the Kenya National Bureau of Statistics' Consumer Price Index, and then converted to 2007 U.S. dollars using the average exchange rate from August 2007.

33

It is important to note that our respondents are not a representative sample of Kenyan workers, so it is certainly possible that average incomes did decline after the crisis but that the impacts were strongly concentrated among older workers or (in Nairobi) those from other ethnic groups—in which case, KLPS2 respondents' beliefs could accurately reflect a change in the average wage that did not have an impact on them.With only one exogenous variable, it is impossible to fully tease apart any causal relationships between outcomes that were directly or indirectly affected by the postelection crisis. Nonetheless, the magnitudes of the relevant coefficients suggest that changes in beliefs about income are not a plausible explanation for the entire observed decline in risk tolerance. The 2SLS estimates (which are larger in magnitude than the OLS estimates) suggest that the crisis lowered beliefs about average incomes by between US$35.41 and US$ 37.42 per month. Beliefs about income are positively associated with risk tolerance in the precrisis period ($p$-value 0.004), but the coefficient is small—US\$ 100 increase in one's belief about the average income is associated with a 0.253 unit increase in our index of risk tolerance. If we treat the precrisis relationship between beliefs and risk tolerance as causal, then a back-of-the-envelope calculation suggests that the postelection violence lowered perceived incomes enough to lower the risk index by about 0.095—but observed changes are at least five times larger than that. Thus, beliefs about income are not likely to be the primary mechanism through which the postelection crisis altered risk preferences. Concerns about the “bad controls” problem notwithstanding, our results are robust to the inclusion of beliefs about income as a right-hand-side variable.

34

It is worth noting that most of the KLPS2 survey enumerators were members of the local-majority Luhya ethnic group. Our results cannot be explained by the decline in trust of other ethnic groups after the crisis. We see the same robust association between exposure to the crisis and increased risk aversion in the subsample of respondents who were interviewed by a member of their own ethnic group.Trust and social capital are unlikely to explain the observed impact of the crisis on risk tolerance because there is no significant relationship between these variables and our measure of risk tolerance prior to the postelection violence.

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## Author notes

We are grateful to the staff at IPA-Kenya for their assistance and support; to Kattya Quiroga Velasco for research assistance; and to Michael Callen, Pascaline Dupas, Marcel Fafchamps, Jonas Hjort, Diego Garrido Martin, Ted Miguel, Anja Sautmann, Adam Wagstaff, Waly Wane, two anonymous referees, and numerous conference and seminar participants for helpful comments. All errors are our own.

The findings, interpretations and conclusions expressed in this paper are entirely our own and do not necessarily represent the views of the World Bank, its executive directors, or the governments of the countries they represent.