The 1990 Cocoa Crisis in Côte d’Ivoire ∗

We look at the drastic cut of the administered cocoa producer price in 1990 Côte d'Ivoire and study to which extent cocoa producers' children suffered from this severe aggregate shock in terms of school enrollment, labor, height stature and morbidity. Using pre-crisis (1985-88) and post-crisis (1993) data, we propose a difference-indifference strategy to identify the causal effect of the cocoa shock on child outcomes, whereby we compare children of cocoa-producing households and children of other farmers living in the same district or the same village. This causal effect is shown to be rather strong for the four child outcomes we examine. Hence human capital investments are definitely procyclical in this context. We also provide evidence of gender bias against young girls with respect to education and health care. We last argue that the difference-indifference variations can be interpreted as private income effects, likely to derive from tight liquidity constraints. two anonymous reviewers and an associate editor for helpful discussions and suggestions, and seminar participants at Oxford (CSAE), London (Brunel and LSE), Stockholm, Clermont-Ferrand (CERDI), Madrid (Carlos III) and Paris (PSE and EUDN annual meeting). The usual disclaimer applies. 1 Introduction In many low-income countries, and in Africa in particular, the majority of the labor force still works in agriculture, whether for subsistence crops or for cash crops. Agriculture is a risky activity: Unpredictable shocks on production on the one hand, exogenous price variations on the other, generate a high volatility of individual incomes. Furthermore, formal credit and insurance markets are very limited, and informal risk-sharing mechanisms within communities can hardly cope with aggregate shocks such as droughts, pests or commodity price falls. Constraints on savings and borrowing not only weigh on households' consumption smoothing but also on their ability to pay for basic investments in their children. On this latter aspect, a large body of empirical research has already examined the multiple determinants of human capital investments in developing countries, like community resources, parental education, or household resources, using structural production functions, reduced form approaches, or a hybrid of the two (Strauss and Thomas 1995). This literature has long recognized the many econometric difficulties raised by the estimation of the causal effect of these determinants , because of the contamination of statistical correlations by unobservables stemming from other simultaneous household decisions (fertility, migration, labor 1 supply), sample selection due to mortality, or endogenous programs' placement. Regarding the effects of household …

tility, migration, labor supply), sample selection due to mortality, or endogenous programs' placement.
Regarding the effects of household income, randomized experiments on conditional cash transfers have recently brought a straightforward answer to this identification issue (e.g., Schultz 2004;de Janvry et al. 2006;Filmer and Schady 2008). Yet the impacts of unconditional and of negative income variations are still not well known, and the African context is less studied. Recent works alternatively exploit the natural experiments generated by macroeconomic crises (Cutler et al. 2002;Schady 2004;Thomas et al. 2004;Pongou, Salomon, and Ezzati 2006). Others focus on agricultural income, whether looking at shocks on production such as droughts (Jensen 2000;Yamano, Alderman, and Christiansen 2005;Alderman, Hoddinot, and Kinsey 2006;Maccini and Yang 2009) or at commodity price changes. The present contribution adds to this latter strand by investigating the impact of a fall in producer price of an export crop (cocoa) on investments in children in an African country (Côte d'Ivoire), whereas former contributions address rather different cases: rice (both a cash and subsistence crop) in Vietnam (Edmonds and Pavcnik 2005) or coffee in Brazil (Kruger 2007) or in Colombia (Miller and Urdinola 2010). Sub-Saharan Africa differs from East Asia or Latin America if only for its low achievements in primary school enrollment, child nutrition, or mortality under age 5.
With all these empirical studies, the first issue at stake is sign identification: does a negative aggregate shock increase or decrease investments in children? As such a shock reduces the opportunity cost of time for children and/or adults, children may work less and parents may have more time left for child care. This substitution effect may dominate the income effect and result in countercyclical human capital investments. The income effect could, however, dominate in low-income countries because of tight borrowing constraints (Ferreira and Schady 2009). The few studies on African cases exhibit procyclical health and education: nutrition worsens and schooling is decreased in times of drought or crop failure (Jensen [2000] for Côte d'Ivoire, Yamano et al. [2005] for Ethiopia, Alderman et al. [2006] for Zimbabwe, and Beegle et al. [2008] for Tanzania). In contrast, in Latin American countries, education is often revealed to be countercyclical (e.g., Schady [2004] for Peru) whereas evidence is mixed for health (procyclical: Cutler et al. [2002] for Mexico; countercyclical: Miller and Urdinola [2010] for Colombia).
A second issue lies in the interpretation of results. Reduced-form analyses show that children are causally affected by shocks but find it more difficult to disentangle the channels through which those shocks exert their impact, in contrast with former contributions based on structural models (see, e.g., Jacoby and Skoufias 1997;Glewwe and Jacoby 2004). Indeed, depending on the context, many determinants of human capital investments can vary concomitantly as a result of the shock, for example, household income, health supply, education returns, or child wages. Limitations in channel identification may arise from the nature of the shock under study, from data availability, or from both. Still, in terms of policy, the attribution of these effects remains of utmost importance, for instance in the design of school fees or safety net schemes (Behrman and Knowles 1999;de Janvry et al. 2006).
Our strategy relies on the natural experiment provided by the unexpected and drastic cut of the administered cocoa producer price in 1990 Côte d'Ivoire. We exploit two data sets from nationally representative large sample household surveys that were implemented before and after the cocoa crisis, in 1985-88 and 1993. First, we show that the cocoa crisis did negatively affect the human capital of cocoa producers' children by comparing them with noncocoa farmers' children, across time, within the same geographical area, and along several dimensions: school enrollment, child labor, height stature, and incidence of illness. Human capital investments are revealed to be procyclical here. Second, we argue that the cocoa crisis did not affect child outcomes through any other channel than household income.
The remainder of this article is organized as follows. Section II presents the background, the data, and our difference-in-difference identification strategies and gives a first overview of our main results. Section III addresses the biases that may affect the estimated impacts of the price shock. Section IV discusses transmission channels and results in detail; it argues that the income effect dominates price effects. Section V presents conclusions.

II. Background, Data, and Identification
A. Background From independence till the 1980s, Côte d'Ivoire has experienced dramatic growth thanks to cocoa exports. Because cocoa is produced by replacing forest trees with cocoa trees, its production is limited to the southern (and forested) half of the country. Coffee is also grown in the same areas, although in much lower volumes, so that the two groups of cocoa and coffee producers very much overlap. 1 The northern savannah region does not produce cocoa at all and instead grows cotton as an export crop. Figure 1 displays a map of Côte d'Ivoire, where administrative districts (départements) and survey clusters (pri- Figure 1. District density of cocoa production and main occupation of survey villages. Sources: CSSPPA (1990), Cô te d'Ivoire Living Standards Measurement Surveys 1985-88, Enquê te Prioritaire 1993 household surveys, and authors' calculations. District density of cocoa production is calculated as district production of cocoa beans in tons (1985-86/1987-88 average) divided by district area in square kilometers. Circles, lozenges, and squares are primary sampling units (PSUs), that is, survey clusters. An occupational group p {nonfarmers, cocoa (farmers), noncocoa (farmers)} is defined as the major group in the PSU if it gathers the highest number of households. mary sampling units [PSUs]) have been categorized according to the importance of cocoa production.
The cocoa producer price was administered by the state-owned marketing board (the Caisse de Stabilisation et de Soutien des Prix des Produits Agricoles [CSSPPA or "Caisstab"]), which fixed it below the international price. The Caisstab never fulfilled its mandate to stabilize international prices and imposed implicit taxes on agriculture. From 1979, the decline in the international cocoa price and the increasing deficits of the Caisstab forced the government to cut the producer price for the first time in 25 years, first from 400 to 250 Communauté Financière Africaine francs (CFAF) per kilogram in June 1989 and then to 200 CFAF in 1990 (see fig. 2). The administered coffee price was also cut from 385 to 200 CFAF at the same time.
The administered cotton price fell only from 115 to 90 CFAF between 1988 and 1993, and staple food prices also decreased but to a much lesser extent than the price of cocoa (between 20% and 30% according to Jones and Ye [1997,[11][12]). The years 1985-88 have been a period of high yields and high prices for cocoa producers, and yields remained high after 1990 (7).
Given these evolutions, between 1988 and 1993 we expect the income of districts producing cocoa to have fallen more than the income of other districts. Likewise, within cocoa-producing districts, we expect the income of farmers who grow cocoa to have fallen more than that of other farmers. This is confirmed by figure 2: cocoa-producing households exhibit a 20% higher level of consumption per capita in 1985-88 but they end up at par with other farmers in 1993. 2

B. Data and Variables
Our main sources of data are the four Côte d'Ivoire Living Standards Measurement Surveys (CILSS) from 1985 to 1988 and the Enquête Prioritaire (EP) 1993, all conducted by the Institut National de la Statistique of Côte d'Ivoire with the support of the World Bank. Although the 1985-88 surveys include a small 2-year rotating panel, we do not make use of this dimension. The 1993 survey is a completely independent sample. Not having a panel running across the preshock and postshock periods raises important identification difficulties that we try to address later on. As we are interested in the comparison of children between the precrisis and the postcrisis periods, we stack all the household data for 1985-88. In the end, when looking at the population of 0-(more than 6 months) to 15-year-old children, we obtain 22,811 individuals in 5,299 households across 200 PSUs or survey clusters in 1985-88 and 26,977 individuals in 7,358 households across 480 PSUs in 1993.
We are able to isolate subsamples of children whose living conditions depend the most on cocoa production and income. First, we can define in a homogeneous way across surveys the group of cocoa-producing households among farming households, whether they are landowners with tenants who grow cocoa trees or landowners or sharecroppers who directly grow cocoa, provided that more than 1 kilogram of cocoa beans have been harvested. Hence we can divide the sample into three occupational groups: cocoa-producing farmers, noncocoa farmers, and nonfarmers. 3 As we shall see later on, the shares of those three groups varied little across the cocoa crisis. Second, the district of birth of each child is reported on the basis of an administrative grid that distinguishes 50 districts; hence we can also break down our children samples according to the density of cocoa production in the district of birth using administrative (hence survey-independent) cocoa production data for the precrisis period . Among these 50 districts, we isolate the 28 southern districts where this density of production is higher than 1 ton of cocoa beans per square kilometer (see fig. 1 above).
We consider four child outcomes. Table 1 provides some descriptive statistics for children living in agricultural households, broken down by cocoa status, gender, and period. The last column of the table provides a first differencein-difference estimate based on the double difference of means.
Our income variable is consumption per capita (at 1988 prices) since consumption is better measured than income in poor countries. We are careful to include the consumption of own food production and imputed housing rent and to exclude very infrequent durable goods acquisition and health expenditures. Income available for consumption corresponds to the ex post income once coping strategies have been implemented to mitigate the ex ante cocoa income cut: an increase in labor, dissaving and sale of assets, borrowing, and so forth. For the whole sample, we estimate real per capita consumption to have fallen by 39% between 1988 and 1993, which is not completely inconsistent with estimates from Maddison (2003) indicating a 27% fall of real GDP per capita. The survey figure is the same for the subpopulation of agricultural households, that is, a 39% drop again. As already seen in figure  2, this consumption per capita fall is more pronounced for cocoa households (see the top two rows of table 1). We acknowledge that consumption figures can be affected by measurement problems. In particular, the official consumer price index (measured in the capital city Abidjan) points to a 9% increase that is little consistent with indications of large falls in producer prices for food staples (Jones and Ye 1997). As our survey estimates are based on nominal values (with also consumption of own food production being evaluated at prevailing market prices), the aggregate consumption fall could be overestimated because of a wrong deflator, if only for agricultural households. Yet as we focus on reduced-form estimates, the measurement of consumption plays no role in our identification strategy. Moreover, as our preferred estimates include district-year or village-year fixed effects, we may think that we control for the spatial variation in the level and the structure of prices so that the difference in difference in consumption per capita is reliable.
Regarding school enrollment, we distinguish two age groups, 7-11 and 12-15, 11 being the theoretical age of completion of primary school. The surveys do not provide information on age of entry into school or curriculum, and literacy is not asked the same way in both surveys. With current enrollment, the month of interview is an issue; for instance, enrollment is underreported in August as it is a period of holidays. We instead use "currently enrolled or enrolled in last 12 months," which does not exhibit seasonality. The first difference-in-difference estimates show that enrollment decreased in cocoa-farming households relatively to noncocoa farmers, especially for girls between 7 and 11 years of age (Ϫ22 percentage points). Enrollment of noncocoa children is strikingly little affected, on average, for all four age-gender groupings, as if it had already reached an incompressible level.
Regarding child labor, we use information on work in the last 7 days for individuals over 7 years of age. 4 Household chores are not included, and more than 95% of reported child labor is employed on household farms. Table 1 suggests that child labor increased between 1985-88 and 1993 among cocoa farmers, mostly for 12-15-year-old boys (from 30% to 40%), whereas it decreased by around 10 percentage points among noncocoa farmers. This latter decrease is partly explained by an increase in underreporting due to a change in the questionnaire between 1985-88 and 1993. The comparability of the two surveys is indeed questionable in the case of the least heavy workloads. 5 We come back to child labor later in Section IV.B.
With regard to health outcomes, height stature is measured in each survey for children between 6 months and 4 years (59 months) of age. For age in months, rounded off figures and missing values are observed as usual in Africa. We construct two types of height-for-age Z-scores using the World Health Organization standards (WHO 2006): observations with missing age in months are given their age in years times 12 plus 6 or else times 12; we also analyze height regressions with controls for sex and age and their interactions. We primarily use the first version of Z-scores and use the other two for robustness checks. We distinguish two subsamples: children from 6 to 23 months (all of them born after the shock) and children from 2 to 4 years. Table 1 shows that height-for-age Z-scores decreased significantly between 1985-88 and 1993 for all groups of children. However, the difference in difference is mostly significant for the 2-4-year-olds.
Furthermore, parents declare whether their child has suffered from an illness or an injury during a reference period preceding the interview; the question is exactly the same in both surveys except that the reference period is the past 4 weeks in the 1985-88 surveys and the past 2 weeks in the 1993 survey. To analyze this incidence of morbidity, we consider two subsamples of children: 6 months to 4 years and 5-15 years. The halving of the reference period explains why morbidity has decreased between 1988 and 1993 in all groups. Our difference-in-difference strategy should correct for this definitional change. It suggests that morbidity increased more among cocoa farmers' children aged 5-15.
Finally, both surveys allow us to gather a large set of control variables regarding the household demographic composition and assets and child and household head characteristics. Those variables are reviewed when used in Section III. 5 In 1993, a question about "professional activity" in the past 12 months comes first, and in practice, very few "inactive" people are then declared to have worked in the past 7 days. Because of this first question, being declared at work is almost incompatible with being enrolled: among 7-15-year-old children, the working ones are only 0.2% likely to be enrolled against 13.4% in 1985-88. However, those figures are exactly the same for cocoa farmers and noncocoa farmers.

C. Difference-in-Difference Identification Strategies
As already stated above, we define a first (and preferred) treatment group, the sample of children living in cocoa-producing households, and contrast it with the sample of children living in noncocoa farming households. Figure 2 confirms that mean consumption per capita has fallen more for cocoa households than for their noncocoa counterparts, by 45% against 33%, although each category has been very much affected by the cocoa-induced macroeconomic crisis.
Alternatively, we can define a second treatment group, the sample of children born in cocoa-producing districts, and a comparison group, the sample of children born in noncocoa districts (defined as producing less than 1 ton of cocoa per square kilometer in 1985-88). When referred to in the literature, this district-level strategy echoes the exploitation of rainfall shocks (Jensen 2000;Maccini and Yang 2009) or price shocks when data on household-level specialization are not available (Kruger 2007;Miller and Urdinola 2010). Consumption per capita evolutions are very close to those obtained with the first cocoa/noncocoa categories: a 41% fall against a 31% fall, even if here nonfarmers contribute to the comparison.
We look at the dynamic relationship between cocoa specialization and household consumption or children outcomes by estimating the following differencein-difference regression model: For each child i observed in area v at year t ( , 1986, 1987, 1988, t p 1985 1993), is the outcome under consideration. This specification holds for all S ivt the reduced-form estimations that are implemented in the remainder of the article, whether for household consumption, child outcomes, or other household-level or child-level variables. Cocoa is a dummy variable indicating whether the child belongs to the cocoa treatment group, that is, depending on the regressions, belongs to a cocoa-producing household or is born in a cocoa-producing district. Cocoa 1993 interacts Cocoa with a dummy for the year 1993. The term X is a set of control variables, including a constant and a time dummy for the year 1993; other variables such as the month of interview can be introduced for robustness checks. For regressions involving our preferred treatment group (Cocoa defined from household-level production), our preferred district and village (survey cluster) fixed-effects specifications include a set of dummies for the area of residence interacted with year in order to control for all factors common to children living in the same area in the same year: .
V vt These district-year or village-year fixed effects are assumed to be common to boys and girls of a given age group and for a given outcome (i.e., 7-11 enrollment, 12-15 enrollment, etc.); hence, in practice the model of equation (1) is estimated by interacting Cocoa and Cocoa 1993 with the gender variable. In all household-level estimations, standard errors are clustered at the level of survey clusters. When district of birth-level estimates are considered, standard errors are clustered at the same level, that is, the district-year level, so as to avoid overoptimistic inference with differences in differences (Bertrand, Duflo, and Mullainathan 2004). Table 2 displays our main results for the same 18 age-gender-outcome combinations as in table 1 and for the same sample of children living in agricultural households. In keeping with the specification of equation (1), the reported estimates include either district-year or village-year fixed effects, and the table reports the coefficients of Cocoa 1993 interacted with the gender of the child (except in the case of consumption per capita). In comparison with the "pooled" double differences in means of table 1 (last column), absorbing place of residence fixed effects significantly attenuates the impact of the shock in the cases of consumption per capita, school enrollment, and child labor. However, fixedeffects estimates still confirm that the crisis was associated with a relative consumption loss for cocoa-producing households, ranging between 8% and 11% depending on the specification. Other figures show that in 1993 the situation of some cocoa children has significantly deteriorated in comparison with others: with regard to education, the 7-11-year-old girls are less often enrolled at school as well as the 12-15-year-old boys, although with less statistical significance. The latter also seem to have been put to work significantly more. With regard to health, 2-4-year-old girls are shorter, and 5-15-year-old boys are more often declared ill or injured. Section IV discusses this series of results in more detail. We do not report estimates based on cocoa production at the district of birth level (see above); while they are pretty much in line with those based on cocoa production at the household level, they are much less precise as they exploit a limited source of variability (50 districts).

D. Main Results: A Preliminary Overview
Our reduced-form results indicate that human capital is procyclical in this context, and they are in keeping with some other works on Africa already reviewed in the introduction. Our two figures about schooling and stunting suggest that the cocoa price shock might have had serious consequences on the "capabilities" of the children living in cocoa-producing households. It is possible that some minimal education was not received and could not be recovered; the same holds for the short stature inherited from stunting in that it reflects an irreversibly diminished health capital. Taking these results as only preliminary and suggestive, we now examine whether our difference-indifference strategy is well founded.

III. Potential Bias of the Difference-in-Difference Strategy
First, we must assess whether we have any indication of exogenous differential trends between our treatment and comparison groups that could account for the evolutions observed. Second, we must check that endogenous composition and selection biases do not contaminate our comparisons across time.

A. Preshock Trends
We first compare district-level school enrollment rates from the 1975 population census and the 1985-88 survey data. We distinguish cocoa districts using the same criterion as for districts of birth between 1985-88 and 1993, that is, the density of cocoa production being higher than 1 ton per square kilometer (as measured in 1985-88). For 6-14-year-old boys, we find that the enrollment rate remains constant, on average, in cocoa districts whereas it increases by 7 percentage points in noncocoa districts. Although the double difference is not statistically significant, it reflects some catching up (when controlling for the initial rate, the difference in trend turns positive although still insignificant). As for girls, the enrollment rates grow, respectively, by 7% and 8% in cocoa and noncocoa districts. Second, we take advantage of the four-surveys structure of our preshock data and use the date of the interview (month-year) to control for preshock differential trends. The period covered goes from February 1985 to April 1989, hence 2 months before the cocoa price shock. We run the same model as in equation (1), but we drop 1993 observations and we include one trend variable T (number of months since February 1985) and its interaction with the cocoa dummy, Cocoa # T: We test for the significance of a preshock differential trend between cocoa and noncocoa farmers, that is, H0: . The variation in month of interview v p 0 reflects the spatial phasing of sample designs within each year, with villageyear fixed effects explaining more than 90% of the month of interview variance; but we check that the same results are obtained when replacing the month of interview trends by year of interview trends. For the five outcomes already studied in table 2 and for the district fixed-effects specification, the full set of estimates are displayed in the top panel of table 3. The bottom panel reports the coefficient ( ) obtained with the other two specifications that Cocoa # T v we already discussed (village-year fixed effects and district of birth estimates).
In the top panel, the third row shows that there is no significant preshock trend for cocoa producers relative to noncocoa producers (i.e., ) for any v p 0 of the four child outcomes. The same results hold for the two other specifications. In the case of log consumption per capita, the positive differential trend obtained with district fixed effects suggests that cocoa households were getting richer (relative to noncocoa households in the same district) during the 1985-88 period. If anything, using the June 1989 projected level instead of the 1985-88 average could lead to reestimating upward the impact of the shock on consumption, with a fall of around 18%-20% against 8%-11% (1), two variables are added: a preshock monthly trend (expressed in years, i.e., number of months divided by 12) using the month of interview, from February 1985 to June 1989, and its interaction with the Cocoa dummy; see eq.
(2) in the text. Cocoa stands for cocoa-producing household. The monthly trend is centered on the month of June 1989. In the top panel, only the constant and district-year fixed effects are not reported. In the two bottom panels, only the coefficient is reported. In the Cocoa # T second panel, the same model with preshock monthly trends is estimated with village-year fixed effects. The third and last panel presents the model with the district of birth-level (instead of household-level) definition of Cocoa and Cocoa 1993 , based on cocoa production density. Standard errors (in brackets) are clustered by PSUs except for district of birth estimates (last row), where they are clustered at the district of birth level. * p ! .10. ** p ! .05. *** p ! .01. without preshock trends. Anyhow, we conclude that there is little support for bias stemming from short-term preshock differential trends.
In the end, the long-term catching-up effect mentioned above leads us to downplay a bit the result on enrollment for boys, even if we feel that this district-level difference in trends could be very much attenuated in the withindistrict dimension, as our shorter-term test suggests (table 3). In contrast, for 7-11-year-old girls, we find little support for either long-or short-term preshock trends that could contaminate our results.

B. Composition and Selection Biases
We study whether other factors than the price and income shocks have influenced the observed difference in difference in outcomes between "cocoa chil-dren" and their noncocoa counterparts. This caution is most important for the estimates based on household-level specialization, as the crisis may have affected the stability (in terms of observables and unobservables) of both our treatment and comparison groups. In contrast, the district of birth-level estimates should rule out this kind of bias: for children of at least 2 years of age born before 1993, the district of birth is predetermined before the cocoa crisis, provided that the price shock was not anticipated. The fact that these latter estimates (available on request), although more imprecise, provide figures similar to household-level ones is quite reassuring.

Occupational Mobility
We first observe that the shares of cocoa and noncocoa households in the total population stayed relatively stable between 1988 and 1993: respectively, 27.5% and 29.2% for cocoa-producing households and 38.7% and 37.1% for noncocoa agricultural households. This means that within the farming households sample, the share of cocoa-producing households increases from 41.5% to 44%. This latter share is even more stable when restricting the sample to districts (respectively, villages) where at least one cocoa farmer and one noncocoa farmer are observed, that is, when dropping northern savannah farmers: 50.7% (56.6%) to 51.3% (57.1%); those latter subsamples are the ones that contribute to the identification of the district-year fixed-effects and villageyear fixed-effects models. We also calculate the share of cocoa households in each village and check that the density distribution of this share did not change between the two years. At the aggregate level, we are thus confident that our two groups exhibit a great deal of stability. This aggregate stability should already limit the potential for selective mobility in or out of these two sectors.
Besides, for households that were already in the cocoa sector before the crisis, it is unlikely that they have given up cocoa, as growing cocoa imposes irreversible investments. A cocoa tree needs 5 years to produce cocoa beans, is mature after 10 years, and may live much longer. A specialist of this sector even noticed some "optimism from cocoa producers" at that time, resulting from several factors (Ruf 1995, 191). First, they had no alternative as profitable as cocoa. Second, they were expecting a price upturn, which indeed happened as soon as 1994. This optimism is confirmed by the fact that many cocoa trees were still being planted. National statistics show that cocoa production and the total area devoted to it did not significantly change between 1988 and 1993. In the case of neighboring Ghana, Hattink, Heerink, and Thijssen (1998) review price elasticities estimates for cocoa production from aggregate time-series data and provide their own using farm-level data: as short-run elasticities range from 0.13 to 0.29, they conclude that price variations have a small effect on resource allocation for cocoa production in the short run. We thus consider that the vast majority of cocoa farmers of 1988 are still in place in 1993, even if they may have further diversified their activities. 6 Yet, these aggregate features do not preclude more subtle compositional changes at the margin, stemming, for instance, from the differential characteristics of new entrants in each sector. This is what we examine now.

Relative Changes in Observables
In order to test for the compositional differences between cocoa and noncocoa households, we look at the set of variables that can be gathered in the surveys and regress each one of them as in equation (1) for the sample of 0-15-yearold children. The coefficients of Cocoa 1993 are reported in table 4 for a subset of these variables and for the two household-level models with district-year or village-year fixed effects. If we take the within-district differences as a benchmark, in the precrisis period, the two groups differ in mean consumption per capita levels, household size (two additional members in cocoa households), and livestock (10 percentage points more livestock owners); besides, the heads of cocoa households are more often men, are uneducated, are nonmigrants, and are older by 2 years. We acknowledge that these differences in mean characteristics could influence the estimated impact of the shock if they command some heterogeneity in households' responses. 7 However, a variation in characteristics is an even greater matter of worry, as it may directly bias the estimated impact even in the absence of response heterogeneity. No significant changes are observed in the case of the districtyear fixed-effects specification (first column of table 4). The only significant differential change is the household head aging by 3.5 years in cocoa households when considering village-year fixed effects. The head's differential aging in cocoa households might be explained by the easier absorption of young households by the noncocoa sector, where entry requires less investment. This investment constraint could be even more binding in time of crisis. However, this mechanism should hold as well for the district fixed-effect comparisons, 6 This is not the case for coffee: after the coffee producer price cut in 1989, many farmers in the forest area stopped producing coffee. Hence the share of coffee producers among farmers went down from 46.7% to 33.1%. Among cocoa farmers, this share went down from 69.9% to 58.0% and, among noncocoa farmers, from 30.3% to 13.6%, i.e., the same compositional shift. 7 For instance, the average cocoa household could have a lower income elasticity than the average noncocoa household, if only because of higher initial wealth. Then the difference in difference will underestimate the response of an "average household" exposed to the same differential income shock: If Y stands for any outcome, X for log consumption per capita, and a for income elasticity, will be higher than by .  whereas it does not significantly do so (it does not either in a pooled specification without fixed effects). We rather conclude that there is some sample variation. As the head's age may still influence some of the four outcomes, we include it as a control variable and check that our point estimates are not altered. We also check that the results of table 2 are unchanged when adding all variables of table 4 (except the first) as controls (results available on request).

Selective Fostering and Endogenous Fertility or Mortality
Cocoa households could have fostered fewer children in 1993 than in 1988 when compared to noncocoa households. The 1985-88 surveys contain a section dedicated to fostered children, from which we learn that, among 2-15year-old children, about one child out of four is fostered and that children are around 5 percentage points more likely to be fostered when they belong to cocoa households. However, this small difference no longer holds when district or village fixed effects are included. Yet, there are no data on fostered children in the 1993 survey, and our identification strategy could be contaminated by some endogenous variation of household composition across time. We examine whether the relative probability of being born outside the district of residence varies over time, which could indicate between-district fostering. We also check whether the likelihood of being the head's biological child varies across time with belonging to a cocoa household. Table 4 confirms that if a change has occurred, it was a very slight and nonsignificant one (see coefficients for "not born in district of residence" and "biological child of the head" in table 4). Besides, the crisis could have increased child mortality relatively more for cocoa households and/or induced those same families to postpone their fertility decisions, which would lead to an endogenous change in the number of young children between cocoa-producing and noncocoa farming households. In the first row of table 4, we examine this possibility by looking at the probability of having a child between 6 and 23 months of age among the sample of 0-15-year-old children. It is indeed in the former age range that we expect child mortality to be the highest; besides, children less than 2 years of age were all conceived after the shock was observed. We also try with other age ranges (0-3, 1-4, and 2-4), and we also test with other comparison groups: 6-15, 6-11, and 12-15. The coefficient of Cocoa 1993 is always close to zero and nonsignificant, suggesting that there is no differential variation in mortality or fertility between our treatment and control groups.
In the end, the examination of potential biases confirms that fixed-effects estimates show great stability in both the demographic weight and the relative composition of the population of cocoa children compared to noncocoa children.

IV. Detailed Results
First, we discuss the price and income effects that could plausibly result from the shock. After arguing that income effects explain most of the observed variations, we implement tentative instrumental variable (IV) estimates of the income elasticity of school enrollment for the sake of comparison with previous attempts in the literature. Second, we turn to a more detailed description of the impacts of the shock.

A. Price and Income Effects
The cocoa price shock had the obvious consequence of tightening the budget constraint of the great majority of Ivorian households, and even more so for cocoa-producing households. Additionally, the cocoa crisis could have modified the prices and costs, whether explicit or implicit, that are relevant when parents decide to invest in their children and again differentially so for cocoa producers. We investigate each one of these price channels and argue that the income effect dominates the results, at least once district or village fixed effects are introduced.

Local Supply and Interactions
We expect the aggregate income of villages with more cocoa farmers to have decreased more. If the provision of public goods is determined at the local level, we expect a relative decrease in the quantity and/or the quality of human capital supply (schools, health centers), hence a relative rise in the cost and shadow price of human capital investments for cocoa farmers. Likewise, a local variation of child and adult wages influences household labor supply, time allocation, and human capital decisions. Nonmarket social interactions also play a role: as some selected families withdraw their children from school or delay their entry, neighboring families can be induced to do the same. However, when including district and even village-year fixed effects, we are controlling for all those channels whose effects are shared by households living in the same area. The inclusion of those fixed effects implies that the only price changes that matter are those differentially affecting cocoa and noncocoa farmers living in the same local environment.

Returns to Education
As the cocoa price falls, the expected returns to education could decrease more for cocoa producers than for noncocoa farmers, even within the same village. This is true as long as cocoa producers invest in education so that their children become cocoa producers and as long as they expect the price shock to be sustained. However, as already mentioned before, cocoa producers remained rather optimistic about the cocoa price prospects. Furthermore, cocoa production is not particularly intensive in human capital. The surveys tell that heads of cocoa households are actually a bit less educated than other farmers. Education is better seen as a strategy to allow children to escape from the agricultural sector or to diversify production activities, so that cocoa and noncocoa farmers should share the same expected returns to education, especially when they live in the same area.

Time Allocation
As the cocoa price falls relative to other export and food crops, both child and adult labor become less profitable in the cocoa sector. With imperfect local labor markets, the child and adult opportunity costs may be different in cocoa households compared to noncocoa households. Cocoa farmers might then reallocate more labor to other activities and/or reduce more labor supply. In this latter case, a price-induced decrease in child labor could be indirectly beneficial in terms of school attendance and health status; likewise, a priceinduced increase in adult leisure could bring more time for child care in cocoa households (e.g., Miller and Urdinola 2010). We do not believe that these substitution effects carry an important weight with our context. First, we already noticed above that national cocoa production has not changed much over the period. Second, the observed reduced-form impacts of the crisis on child labor are either positive or null, not negative: on average, older children (12-15 years old) of cocoa households seem to significantly increase their labor participation whereas the youngest (7-11) do little (see table 2). Indeed, households mainly use child labor as insurance (e.g., Jacoby and Skoufias 1997). Third, we implement the same test for adult labor by estimating equation (1) for 18-60-year-old individuals. The 1993 survey does not provide for the hours worked by either children or adults, so that our analysis is confined to the discrete decision of labor participation. We detect no significant variation in adult participation in the district or village fixed-effects specifications and rather a slight increase in the pooled estimates. Then, even if the relative price decrease has a substitution effect on time allocation, it is very much counterbalanced by the income effect, which plays in the opposite direction.

Income Effect
In the end, we believe that our differences-in-difference estimates with district or village fixed effects capture a true income effect, like the one that would be observed in a virtual field experiment whereby a significant amount of income would be unconditionally withdrawn from the pockets of randomly selected households. Although we cannot prove it directly, we believe that this income effect mainly goes through the liquidity constraint channel: when confronted with an income shortage, families cannot pay for more or better food, schooling, or health costs, whatever the coping strategies they implement (including child labor). In the case of school enrollment, we can illustrate the weight of liquidity constraints by looking at educational expenditures in 1985-88. We isolate cocoa-producing households and divide them into five consumption per capita quintiles. Among each quintile, we have individual expenditures for each child and we can compute the average level of educational expenditures for each of the two age groups we consider. We find that the cost of an enrolled 7-11-year-old ranges from 2.8% to 1.2% of mean cash expenditures when going from the poorest quintile to the wealthiest (1.7% on average) or else from 36% to 13% of mean cash expenditures per capita. Costs for a 12-15-year-old child are 50% higher, from 5.1% to 1.8% of mean cash expenditures (3.0% on average). For both age groups, the bulk of those costs is made up of books (for more than 40%) and uniforms (around 20%) followed by boarding costs (more than 10%) and contributions to parental associations and fees (both around 5%). Cocoa households have, on average, around two children at school between ages 7 and 11 and about one child between 12 and 15, so that total school expenditures weight between 11.1% and 4.4% of cash expenditures (7.0% on average), or between 7.3% and 3.2% when dividing by total consumption instead. Hence, given the magnitude of the cash income shock generated by the halving of the cocoa price, it is fairly probable that some cocoa households, in particular the poorest, have considered saving on schooling costs in order to cope with the income shock.
Assuming that the private liquidity constraint is overwhelming, tentative IV estimates of the income elasticities of child investments can be computed. Those IV estimates are meant to provide a money-metric benchmark for the comparison with other shocks examined in the literature having different magnitudes and occurring in different contexts. We present those estimates only for school enrollment. According to table 2, the cocoa price shock has decreased the school enrollment of 7-11-year-old cocoa girls by 10 percentage points, on average, with district fixed effects and 9 points with village fixed effects. If all this variation can be attributed to a private income effect, we can compute the double least-squares estimates for the corresponding income elasticity: we regress school enrollment on log consumption per capita, the latter being instrumented by the Cocoa 1993 dummy. We obtain a rather large 0.65 elasticity with district fixed effects and 0.49 with village fixed effects. 8 These IV estimates reach about four times the value of the ordinary least squares estimate obtained by simply regressing school enrollment on log consumption per capita. This points out the existence of strong downward biases affecting the correlation between consumption per capita and school enrollment. These computations of the school enrollment income elasticity show the same orders of magnitude as previous results in the literature. In a different context (i.e., 10 villages of semiarid India between 1975 and1978) and with panel data estimation including village-season-year dummies, Jacoby and Skoufias (1997) get 0.32 for the income elasticity of school attendance of 5-18-year-old children. Likewise, looking at the school enrollment of 10-18year-old Vietnamese children between 1993 and 1998, Glewwe and Jacoby (2004) recover income elasticity estimates ranging between 0.20 and 0.40. Much closer to our work, Jensen (2000) studies changes in enrollment for Ivorian children between 1986 and 1987 using the same surveys as our precrisis data. He distinguishes children living in regions hit by an adverse rainfall shock. He finds that enrollment rates declined by 20 percentage points for 7-15-year-old children in shock regions relative to children in nonshock regions; relative income per capita falls by around 30%, so that the enrollment figure corresponds to a Wald estimate of income elasticity of about 0.66. 9

B. School Enrollment and Child Labor
Here we comment on the district and village-year fixed-effects differences in differences (table 2) in more detail. In the absence of panel data we have no direct way of identifying whether declines in enrollment are due to delayed entries or dropouts and whether children who are put to work are withdrawn from school. The results obtained, however, convey a rather consistent story.
Starting with young kids (7-11 years old), table 2 reveals that only girls are less often enrolled at school, by 9-10 percentage points on average. No difference is found between the 7-8 and 9-11 age ranges (results available on request). For these young girls, we can presume that enrollment is delayed or canceled because of the direct costs of schooling, whereas households protect more the enrollment of young boys. Bommier and Lambert (2000) find that Tanzanian girls enter school earlier but still have lower schooling duration; their interpretation of parental behavior involves the opportunity cost of delaying the girls' marriage. According to this interpretation, delayed enrollment could result in a shortened school curriculum for girls who were aged below 11 at the time of the shock. Besides, evidence from other surveys and from the field indicates that cocoa bean harvesting is more a male task, whereas plantains are more a female crop (see, e.g., Doss [2002] on Ghana); the fact that cocoa cash income is more a male income could play a role here if fathers have a preference for sons over daughters. Finally, young kids (7-11 years old) do not work more: less than 15% of them worked in cocoa households initially; they are probably too young to be put to work significantly.
After age 12, conversely, boys seem to be hit whereas girls do not, both in terms of enrollment (by 8-9 points) and in terms of labor (by 14-16 points). Let us first discuss this absence of impact on girls and the gender difference.
Girls younger than 12-15 are enrolled less (22-percentage-point difference) and already work more often (12-point difference) than boys in 1985-88 cocoa households. Hence, there is less scope for decreasing their enrollment or increasing their workload. Still, one may wonder whether the insignificant increase in labor can be the combination of a price effect and an income effect of opposite signs. However, as just mentioned, cocoa is more a "male crop." Besides, aggregate cocoa production did not decrease, so that we believe that girls were not massively drawn out of cocoa harvesting. Finally, it should also be remembered that household chores cannot be included in our definition of labor, whereas they concern more girls than boys. Beegle et al. (2008) study the impact of crop shocks on 7-15-year-old child labor in Tanzania and find an increase in agricultural work for boys but an increase only in chore hours for girls; they argue that this additional child labor affects schooling only in the case of boys, for chores are more compatible with school attendance. They also find girls to be married earlier. Consistently enough, Edmonds (2006) finds that South African 13-17-year-old boys benefit more from a positive income shock in terms of school enrollment and hours in market work, even if girls also benefit in terms of decreased chore hours. Hence, in our case, perhaps some of the 12-15-year-old girls who were already enrolled were kept at school because they were closer to the age of marriage (bride-price effect) while doing more chore hours that we cannot measure. Anyhow, this lesser reduction in enrollment of girls does not cancel out the gender bias: even in 1993 and within cocoa-producing households, 12-15-year-old boys are still more often at school than girls of the same age, by 16 percentage points (55% vs. 39%; see table 1); they end up at par with girls in terms of labor, whereas the latter do presumably more chores.
For 12-15-year-old boys, reduced enrollment could be directly linked to increased labor, whether from more children at work or from more hours worked per child. However, the catching-up trend of noncocoa boys that we identified in Section III.A leads us to look at the enrollment decrease with caution. Besides, as emphasized in Section II.D, the interpretation of the child labor impact is made harder by comparability issues since the 1993 survey underreports the least heavy workloads. Let stand for heavy workloads ϩ W (incompatible with school enrollment) and for light workloads that are Ϫ W not recorded in 1993. Assuming that underreporting is not different between cocoa and noncocoa households, the difference-in-difference estimates measure . They provide a reliable es- Cocoa,1988Noncocoa,1988 timate of the relative increase of heavy workloads in cocoa households if and only if light workloads are as frequent in cocoa and noncocoa households before the shock: . We have no direct measure for in Cocoa,1988Noncocoa,1988 1985-88. Yet, if we define as the combination of working and going to Ϫ W school, we find that 6.0% of 12-15-year-old children are in that case within cocoa households in 1985-88 and 8.0% within noncocoa households, the bulk of the difference stemming from boys (7.1% vs. 11.4%); even with district or village fixed effects, the difference between cocoa and noncocoa is small and insignificant. Thus, the figures for girls should not be affected by this potential bias. Conversely, the increase in "heavy" child labor for 12-15-yearold boys could be biased upward by around 4 percentage points. This number is, however, very much below the 13.6% or 16.0% increases that we obtain with either district fixed effects or village fixed effects. When we computed the difference-in-difference estimates for the "worked and was not enrolled" dummy variable, the results changed little: 13.2% and 12.4% increases, respectively, for 12-15-year-old boys. 10 We therefore conclude that boys have experienced a significant increase in labor, even if we cannot safely link it to a fall in enrollment.

C. Height Stature and Illness
Children between 2 and 4 years of age living in cocoa households have relatively lost between 0.25 and 0.62 international standard deviations in height-forage. This impact is rather large. It is robust to an alternative imputation of missing age in months and is also maintained when height is directly analyzed (with age in months interacted with gender controls). 11 Table 2 indicates that young girls are a bit more affected than boys. This gender inequality is consistent with the results of Friedman and Schady (2009), who find that girls' premature deaths are twice as sensitive to GDP variations as boys' in sub-Saharan Africa; it is not consistent with the results of Yamano et al. (2005), who find that crop failures in Ethiopia affect more boys' nutrition at early ages (6-24 months). Then, we do not find any visible impact on children aged from 6 to 23 months. However, this does not mean that those younger children did not reveal stunting later on. We have indeed good reasons to think that the scarring effect of the shock could be blurred in this population. First, nutritional differences are better revealed at the childhood stage (ages 2-4) when children are no longer breast-fed and height velocity stabilizes (see Bogin 1999, 67-79;Moradi 2010). Second, as we are studying a persistent 10 Apart from the number of children at work, the increase in the number of hours worked per child, i.e., of heavy workloads, could also be responsible for the drop in enrollment. Unfortunately, the 1993 survey does not report work hours. 11  income shock, the duration of exposure to bad living standards can matter. The great majority of the 2-4-year-old children have been exposed to the cocoa shock since birth; hence we can say nothing about the timing of the scarring effect, in contrast with Maccini and Yang (2009), who relate rainfall in the year of birth to height stature as an adult. 12 As our result holds with village fixed effects, it cannot be attributed to changes in the infectious environment but rather to lack of health care and to worsened nutritional conditions. The income shock directly affects the drugs or food that households can afford to buy, and the increase in the work effort of other members may require more food intake that competes with the food left available to the youngest. Table 2 also confirms the increased incidence of morbidity among 5-15year-old cocoa children compared to their noncocoa counterparts: cocoa children are more often declared ill or injured by 3-4 percentage points. We would have thought that the heavier workload of 12-15-year-old boys would have a direct influence on their morbidity, but we do not find such a result. Besides, no effect is found for children aged 6 months to 4 years. As younger children are twice as often declared ill (see table 1), this missing impact may be attributed to the coarseness of our discrete indicator, whereas a continuous variable such as height-for-age Z-score is more able to capture the deterioration of health conditions at early ages. Noticeably, the naive correlation of this variable with income is positive, as is often found with health self-assessments: rich parents are more able to recognize symptoms and overreport that their children are ill, whereas poor parents lack knowledge about illness or are more used to suffering and underreport. With our difference-in-difference strategy, this correlation of permanent components of household income with selfassessments of child health is canceled out.

V. Conclusion
African economies remain little diversified and vulnerable to changing international prices. In Côte d'Ivoire, the largest cocoa-producing country in the world, more than 25% of the population produces cocoa and is directly affected by fluctuations in the price of this commodity. The rest of the population is also indirectly concerned, through market and nonmarket linkages. Formal and informal credit and insurance being limited, farming households find it difficult to cope with aggregate shocks such as droughts, pests, or commodity price falls. Those constraints weigh in particular on their ability to pay for basic investments in their children.
Here we look at the drastic cut (Ϫ50%) of the cocoa producer price in 1990 Côte d'Ivoire and study how cocoa producers' children suffered from this severe aggregate shock in terms of school enrollment, labor, height stature, and morbidity. Using precrisis  and postcrisis (1993) data, we propose a difference-in-difference strategy to identify the causal effect of the shock on child outcomes whereby we compare children of cocoa-producing households and children of other farmers living in the same area. This effect is shown to be rather strong for our four child outcomes. Hence human capital investments are definitely procyclical in this context. We also provide evidence of gender bias against young girls with respect to education and health care. We argue that the difference-in-difference variations can be interpreted as an income effect, likely to derive from tight liquidity constraints: parents would like to invest in their children but cannot afford to.
In the past, the national marketing board for cocoa, the Caisstab, did not serve its original mission to stabilize the cocoa price but was rather used to tax the agricultural sector; it was dismantled in 1998. Nevertheless, new insurance schemes and safety nets could be invented to protect households and children from unexpected negative income shocks. If one believes the estimates presented here, those programs might constitute a defendable use of foreign aid money.