Abstract
In 2010, primary school in Malawi began in September, three months earlier than in 2009. I show that this change forced households to sell crops early, when prices are low. The effect is limited to households with school children, increases with the number of children, and is present only for poor households. Households that financed school by selling early missed out on an expected 17.3–26.5 percent increase in output prices over three months. There is little evidence of improved schooling outcomes as a result of the change. I discuss the implications for policies that offer farmers commitment opportunities at harvest.
I. Introduction
Crop prices in sub-Saharan Africa exhibit substantial seasonal fluctuations. The nominal prices of some crops increase by as much as 50–100 percent from a harvest-season trough to the lean-season peak (Burke, Bergquist, and Miguel 2019; Kaminski, Christiaensen, and Gilbert 2014). These largely predictable price cycles offer farmers a profitable opportunity. Those who can delay selling crops until prices rise during the lean season enjoy returns that often exceed those available through savings groups or other financial mechanisms (Alderman and Shively 1996).
Despite this intertemporal arbitrage opportunity, a broad concern of researchers and policymakers is that liquidity-constrained farmers may sell crops early to finance expenditures that arise before crop prices reach their peak. In a sample from Kenya, Stephens and Barrett (2011) find that credit constraints are at least partly responsible for the “sell low, buy high”phenomenon, with households in the lean season buying back the same crops that they sold earlier in the year. For these households, the crop market effectively represents an expensive source of finance. Recent experimental work has shown high uptake and positive impacts from providing credit or storage technologies to lower the cost of moving wealth across time (Burke, Bergquist, and Miguel 2019; Basu and Wong 2015; Fink, Jack, and Masiye 2020).
In this work I use a natural experiment from Malawi to test the hypothesis that shortterm expenditure needs force poor households to sell crops early, when prices are low. The experiment is from a change in the primary school calendar. In 2010, the government mandated that the school year switch to a September start date. This was three months earlier than the December start date of 2009 and four months earlier than the January start date of the previous 15 years (Frye 2011; Milner, Mulera, and Chimuzu 2011).
Section II provides details about the policy change. One of the government’s reasons for moving school to September was to bring it closer to the harvest, thereby increasing the capacity for farming households to pay school costs. Although there is no primary school tuition in Malawi, households incur out-of-pocket costs in the form of informal fees, voluntary contributions, and purchase of supplies and uniforms. The change in the school calendar introduced a sharp change in the timing of these expenses relative to the crop price cycle. Importantly, the change was accomplished by shortening the school year, rather than shortening the break period. This helps me rule out alternative explanations related to the opportunity cost of child time during critical periods of agricultural work.
Section III develops the empirical approach in the paper, which combines the difference-in-difference (DID) strategies of Card (1992) and Hamermesh and Trejo (2000). Here, one dimension of difference is the year, and the other is the number of primary school–aged children in the household. In the main analysis I restrict the sample to agricultural households below the poverty line, who represent approximately half of all farming households, because these households are the most likely to be credit-constrained. In robustness checks I verify that other reasonable proxies for credit access lead to similar conclusions.
Section IV describes the sample and data. The primary data source is the Integrated Household Survey 3 (IHS 3), collected by the Malawi National Statistical Office. The nationally representative IHS 3 was conducted over a full calendar year, March 2010 to March 2011. The empirical strategy is made possible by a specific feature of the data collection. Households interviewed in the first few survey months could not provide details about sales of crops harvested in 2010 because cultivation was still underway. These households reported their crop sales for the 2009 harvest. Households interviewed from roughly July 2010 onwards were asked to report sales based on their 2010 harvests. I verify in Section IV that this induced geographically stratified, quasirandom variation in “treatment,” where the treatment is the selling of crops in the year that school began in September.
Section V presents the main findings. Difference-in-difference results show that the cumulative value of household-level sales made before September was significantly higher in 2010 than in 2009. This effect is only present for households with children in primary school, and is increasing with the number of such children. For completeness I also estimate triple difference specifications that add a comparison of poor to nonpoor as the third dimension of difference. The triple difference estimates confirm the DID results. Section V also contains an analysis of parallel trends prior to 2010, using an earlier wave of IHS data, and a falsification test using data collected six years after the policy change. The results of both provide support for the validity of the main findings.
The specificity of the effect and the exogenous nature of the identifying variation lend confidence that the calendar change caused the change in the timing of sales. When I vary the month through which I measure the cumulative value of sales, I find the expected pattern if the effect is causal. The difference-in-difference disappears by December, when households in 2009 catch up to 2010 households, and turns (weakly) negative by February. The positive effect early on is from 2010 households selling crops to pay for school; the weakly negative effect in February is from the reduction in the cumulative value of total crop sales over the season, due to the early selling of some crops at lower prices. While the data do not indicate exactly when school costs are paid, the fact that the negative difference-in-difference appears in February suggests that some school-related expenses are spread out over the first two months of the school year.1
The causal interpretation is further strengthened by the similarity between the perchild change in crop sales and per-child cost of schooling. I estimate that before September, poor households sold crops valued at 1,271 Malawi kwacha (MWK) more per child in 2010 than in 2009. The average per-child cost of primary school is 719 MWK in public schools and 1,657 MWK across all schools.
Section VI presents a number of extensions. One is to calculate the opportunity cost of selling early. Using either market price data or farmgate prices, and accounting for depreciation during three months of home storage, I estimate that households lost out on an expected 17.3–26.5 percent increase in crop values over the last quarter of the year. This implies that by selling early poor households lost 217–625 MWK (1.50–4.30 USD) per child in forgone revenues, which is similar to the average direct cost of primary school for poor households. The total penalty incurred by households with multiple children in primary school could be large enough to have serious negative welfare consequences.
That point notwithstanding, the modest size of the effect highlights an important aspect of the findings. Facing earlier school expenditures, poor households chose to forego 17.3–26.5 percent expected increases in crop values—representing annual interest rates of 69–106 percent—rather than finance the outlay through some other mechanism. The implication is that the cost of financing this modest outlay through other means would have been greater than 17.3–26.5 percent per quarter.
I also examine whether the calendar change generated benefits, through improvements in school quality or increased enrollment. Trends in these outcomes following the calendar change are mixed, at best. Literacy among girls improved steadily both before and after the reform; for boys, it fell slightly after 2010. The average student-to-teacher ratio fell after 2010, but the number of classes held in temporary structures increased, and the coverage rate of school feeding programs decreased slightly. Hence, while I cannot rule out that schools improved, I find little suggestive evidence that they did.
Furthermore, after 2010, per-child school payments by poor households grew much faster than those by the nonpoor. This suggests that the policy had the desired effect of increasing contributions from those who previously paid the least. Yet, there is no indication that this led to increased enrollment—enrollment grew faster in the six years before 2010 than in the five years after.
In broad terms, this work makes two contributions. The first is to measure the negative welfare consequences from storing wealth in the form of crops that fluctuate seasonally in value. Seminal papers in development economics have established the importance of nonfinancial ways of storing wealth (Binswanger and Rosenzweig 1986; Fafchamps, Udry, and Czukas 1998), but there are few well-identified estimates of the associated welfare costs. I find that the average lower bound on the cost of capital is 69–106 percent per year, indicating substantial welfare costs to using crop storage as a financial tool.
The second contribution is to provide further insight into the welfare effects of policies that change the timing of economic activities. An important line of work has examined how risk and poverty alter the timing of farm investments and labor market participation (Fafchamps 1993; Kochar 1999; Jayachandran 2006). Recent work has shown the potential benefits of commitment devices to households in low-income countries (Ashraf, Karlan, and Yin 2006; Duflo, Kremer, and Robinson 2011; Liu et al. 2013; Casaburi and Willis 2018). A key finding in that literature is that offering farmers opportunities to commit to future investments by paying for them soon after harvest can be welfare-enhancing (Duflo, Kremer, and Robinson 2011). This is an intuitive, important insight. Harvest revenues that are pre-spent on future investments are not available for overconsumption due to present bias, and they are less likely to be taxed by friends and family (Baland, Guirkinger, and Mali 2011; Jakiela and Ozier 2016; Dillon, De Weerdt, and O’Donoghue 2021). The school calendar change under study here is effectively an extreme form of such a timing policy. The critical differences between this policy change and that suggested by the findings of Duflo, Kremer, and Robinson (2011) are that (i) the earlier school start was not optional since all households were required to start in September, and (ii) the policy affected the entire country simultaneously, straining the informal credit markets that households might have otherwise used to finance school costs. By making the earlier payments mandatory, this policy reduced the real wealth of many poor households over the course of the year.
Of course, all commitment devices have costs, by design. What I show here is that for agricultural households in economies with incomplete financial markets and highly seasonal crop prices—and there are tens, if not hundreds, of millions of such households across sub-Saharan Africa—the real costs of commitment are greater than they first appear because the opportunity cost of liquidity changes substantially across the year. The unintended consequence of the calendar change was to force some households to finance their payments at an annualized borrowing cost of 69–106 percent, with little evidence of offsetting benefits. If the government or some third party could have borrowed at better rates, then the calendar change was an inefficient and seemingly regressive way to increase school funding.
II. Background
This section provides background details for the motivating question and empirical approach in the paper. I cover two topics: the school calendar change that provides the natural experiment used for identification, and the annual crop price cycle in Malawi.
A. The School Calendar Change
Before the mid-1990s, the primary school calendar in Malawi ran from September to July. In 1994, during a wave of policy changes following Malawi’s first multiparty elections, the Ministry of Education changed the school calendar to run from January to November. This change was precipitated by a series of droughts in the early 1990s that forced boarding schools to delay opening in September. The switch to January aligned the start of the school year with the early part of the primary rainy season, minimizing drought risk, and also matched the school calendar of some neighboring countries (Milner, Mulera, and Chimuzu 2011).2
In 2009, the Ministry of Education decided to return the calendar to the September–July schedule (Frye 2011).3 A number of reasons were given for the change: boarding school water shortages had become less of a concern; the change aligned the school calendar with the government fiscal calendar, which was helpful for budgeting; a September start matches the school calendar in the United States and Europe, which benefits those who wish to study outside of Malawi;4 and, finally, the government explicitly noted that moving the start of school closer to the harvest would increase compliance with school fee payments because farmers have more cash in August–September than in December–January (Milner, Mulera, and Chimuzu 2011). Although primary school is technically free, payments from families are important for uniforms, books, other materials, and various school costs and development projects (see Section IV.B for details).
The school calendar change was instituted in two steps. In 2009, classes began on January 5, in line with the standard practice of the previous 15 years. The next school year was treated as a transition year, with school beginning on December 7, 2009, one month earlier than usual. Finally, in the fall of 2010, the school year began on September 6, a full three months earlier than the year before. It is this switch, from a December 2009 start to a September 2010 start, that provides the identifying variation for the study. Importantly, the change was implemented by reducing the number of months of instruction, not by shortening the break. A shorter summer break would raise the prospect of a second channel of influence on agricultural outcomes, via the opportunity cost of child time during the harvest period.
In light of the gradual nature of the adjustment and the transition start date in December 2009, it is safe to assume that this change did not take anyone by surprise. I cannot rule out that some households may have adjusted their labor supply or crop choices to accommodate the new school year cycle. Yet such adjustments, if they exist, would only attenuate the effects that I estimate below. The predictable nature of the calendar change also affects how to interpret the findings. This was not a shock, akin to an illness or accident. Rather, it was a foreseeable change in the timing of future expenditures for households with school-aged children. Whether or not all households had the financial wherewithal to smoothly accommodate this change is part of what I am studying.
The policy reforms of 1994 ushered in another change to the educational system: the abolition of primary school fees. Families have not paid primary school tuition since 1994. However, there are still costs associated with schooling. Students’ families pay for uniforms, books, and stationery supplies, and they are asked to pay informal fees as contributions toward building construction and maintenance (see Section IV.B). Although I do not know exactly when these expenses are paid, many are incurred at the beginning of the school year. In fact, the exact timing within the year does not matter for the identification strategy. The key is that the calendar change moved up the timing of all school costs by three months. If costs are spread throughout the year, then one could see statistically significant differences persist beyond January (though in practice I do not).
B. Crop Price Cycles
Like most countries in sub-Saharan Africa, Malawi has a main rainy season that governs the agricultural cycle. Farmers plant from late November through January. The primary harvest period begins in late April and continues into July. The prices of staple grains and other annually marketed food commodities are lowest at harvest, and rise steadily over the ensuing six to ten months. At their lean-season peak, prices of major food crops may be 50–100 percent higher than at harvest. This annual price cycling of staple food products is common in sub-Saharan Africa (Burke, Bergquist, and Miguel 2019; Kaminski, Christiaensen, and Gilbert 2014).
The upper left panel of Figure 1 plots the average wholesale prices of maize, rice, and beans in markets across Malawi, by month, for 1999–2012. Prices are in nominal terms. There is a clear upward trend in prices over the period shown. Also clear is the substantial intra-annual variation, with short-term peaks occurring in January or February of each year, when the lean season is nearing its worst point.
Notes: Author’s calculations using nominal price data from the Malawi Ministry of Agriculture. In the upper left panel, prices are average, nominal, monthly wholesale prices from all markets with nonmissing data. In the other three panels, percentage increase is calculated with reference to the price in the most recent June. Data for rice and beans are only available for the period 2005–2012. The bars show 90 percent confidence intervals.
To highlight the degree of intra-annual price volatility, Panels B–D of Figure 1 show the same data as the percentage change in prices since the most recent June. The annual cycle is highly pronounced. In February, maize prices are more than 80 percent higher than in June, bean prices are 40 percent higher, and rice prices are more than 30 percent higher. Because these are nominal data that have not been de-trended, some of the intraannual increase is driven by long- term price trends and inflation. However, that is the appropriate framework for motivating the problem that households face because school expenses are set in nominal terms and paid each year. I am interested in understanding whether a shift to paying school-related expenses three months earlier forces farmers to sell crops when prices are lower. Thus, the relevant comparison is a within-year comparison between nominal revenues from selling before September and selling before December.5 The implication of Panels B–D in Figure 1 is that the penalty for selling crops earlier is substantial. Section VI demonstrates that to the extent one can observe them, farmgate prices of maize exhibit intra-annual cycles that match the market price cycles in Figure 1.
Of course, households do not have to sell crops early if they can finance schooling expenses through other means. Households with savings, other regular income, or access to credit may be able to pay for school and also delay selling crops until prices rise.
III. Empirical Approach
I now turn to the empirical setup. The main hypothesis of the paper is that the school calendar change forced poor households in Malawi to sell crops earlier than they would have otherwise. I test this hypothesis by comparing the cumulative value of crop sales through various months in 2009 with the cumulative value of crop sales through the same months in 2010. The effect of the calendar change on a household is a function of the number of children in primary school. Hence, I use the number of primary school children as a treatment intensity margin.
As described in the data section to follow, I randomly observe some households in 2009 and others in 2010, but none in both years. In the main specification I restrict attention to households below the poverty line, out of concern that trends in agricultural and educational outcomes may be different for poor and nonpoor households. In robustness checks I consider alternatives to the poverty line for distinguishing potentially credit-constrained households from households with access to other sources of finance. The pattern in those robustness checks provides strong support for the main conclusions in the paper (Online Appendix D).
Inference about my main hypothesis is based on a difference-in-difference specification in which the first dimension of difference is between 2009 and 2010, and the second dimension is between households with varying numbers of children in primary school. Approximately two-thirds of poor households have children in primary school, so most of the identifying variation is from the intensive margin, not from a comparison of households with primary school children to those without. This use of the intensive margin to identify a DID follows the model of Card (1992), while the comparison between successive, randomly sampled cross-sections follows the approach of Hamermesh and Trejo (2000).
The dependent variable is the cumulative value of crops sales through month m, where m varies from July to February. For 2009 households, this variable includes the value of all sales that take place from harvest (roughly June) through the end of month m in year 2009 or early in 2010. For 2010 households, it includes the value of all sales from harvest to month m in 2010 or early in 2011. I use the value of crop sales as the key outcome, rather than the percentage of output sold, because the sales value better reflects the underlying problem. The start of the school year introduces a set of costs that act as a payment target. If households are indeed selling crops to pay these costs, this should be most closely reflected in the level value of sales per primary school child. Nevertheless, in robustness checks I verify that the findings are robust to reestimation in percentage terms (Online Appendix C).
In our main specification I set m to August. This covers all crop sales that occur up to the week that primary school begins. I could just as easily use the cumulative value of sales through the end of September or October (and I do so, in subsequent analyses). I prefer the end of August for the main specification because it is just before the start of school, and I do not know when in the first weeks of the school year the majority of expenses are incurred. Regardless of the exact cutoff month used to define the dependent variable, the key is that households in 2010 had to arrange to pay school costs three months earlier than in 2009.
The estimating equation for the difference-in-difference is as follows:
1where h indexes households, 
is the cumulative value of crop sales through the end of month m, Childrenh is the number of children in primary school, 2010h is a dummy variable for whether the household reports crops sales for 2010, Xh is a vector of household and location control variables, and εh is a mean zero, i.i.d. error term. I count a child as “in primary school”if (i) the child completed any primary school grade other than the last (Grade 8) in the previous school year, or (ii) the child is six years old and did not attend school the year before because they were “not old enough yet”(as indicated in a survey question). In our main specifications, Xh includes a detailed set of age and gender demographic variables to ensure that comparisons between poor households with different numbers of primary school children are not picking up other effects from differences in household composition.
In Equation 1, the coefficient of interest is β3, which is positive if the calendar change increased crop sales for households with children in primary school. Our central hypothesis is that β3 is positive for poor households, which I implement by testing H0: β3 ≤ 0 in regressions that are limited to households below the poverty line.6
For completeness I also estimate triple difference specifications that compare the change in outcomes for poor households (with varying numbers of children) to the change in outcomes for nonpoor households (with varying numbers of children). The estimating equation for the triple difference is as follows:
2where Poorh is a dummy variable indicating whether the household is in poverty (which is almost exactly equivalent to being below median expenditure per capita), and other variables are as above. The coefficient of interest is β7, on the triple interaction term. The hypothesis that the calendar change forced poor households to sell crops earlier is represented by a test of whether β7 is positive.
In all specifications I cluster standard errors at the level of the enumeration area, which is roughly equivalent to a village. This is the level at which survey timing was determined, and thus the level at which households reported either 2009 or 2010 crop sales. Clustering at the level of the enumeration area helps mitigate potential effects of recall bias. Relative to their respective harvests, households reporting their 2009 crop sales were interviewed on average a few months later than those reporting their 2010 crop sales. There is no direct way to determine whether this led to differences in recall bias because simple between-year difference in agricultural outcomes could arise for many reasons. However, if recall bias is responsible for any of the between-year variation in the dependent variable, the difference-in-difference framework allows the average value of sales to vary across years, which controls for any level differences due to recall, and clustering standard errors at this level allows the conditional variance of sales to vary across enumeration areas and therefore across recall periods. Hence, this approach is robust to any differences in recall bias that affect the first or second moment of the crop sales distribution.
IV. Data, Sample, and Descriptive Statistics
This section describes the data, sample, and descriptive statistics. I provide summary statistics separately for the independent variables, school expenses, and crop sales.
A. Data and Sample
The primary data for this study are from the Third Integrated Household Survey (IHS 3) collected by the National Statistical Office of Malawi. This survey is part of the multicountry Living Standards Measurement Study—Integrated Surveys on Agriculture (LSMS–ISA) project, organized by the World Bank. Data collection began in late March 2010 and continued for a full calendar year. The questionnaire spans a wide range of topics, including demographics, health, education, time use, finance, income, consumption, agriculture, and others.7
The IHS 3 sample was drawn in two stages.8 The first involved random selection of enumeration areas (EAs), stratifying on district and urban/rural status. The EAs are roughly equivalent to villages or to large urban neighborhoods. Malawi has 28 districts, and 24 EAs were chosen per district, with the selection probability based on the EA population in the 2008 census.9 This step generated a sample of 768 EAs. Again stratifying on district and rural/urban status, a randomly chosen subsample of 204 EAs were then designated for the “panel sample”; the remaining 564 were designated for the “cross-sectional sample.”
In the second sampling stage, within each selected EA, 16 sample households and five replacements were randomly selected from the local census listing maintained by community leaders. The team visited panel households twice, once before and once after the 2010 harvest, and also designated this group for followup surveys in future years (the first of which occurred in 2013). The team visited each cross-sectional household once, with no intention of followup. After dropping 17 panel households that were not interviewed during the second visit (at which point replacement was not possible), the final sample consists of 9,024 cross-sectional households and 3,247 panel households.
To account for spatial and intertemporal variation in consumption, prices, and agricultural outcomes, the interview dates for cross-sectional households were randomized over the span of a year, from late March 2010 to early March 2011. Randomization was at the EA level. This interview schedule enables our identification strategy because it introduced random variation in the harvest year for which households report crop sales. The large majority of cross-sectional households interviewed in March–July 2010 could not provide information about the 2010 harvest because it was not complete yet. Hence, these households were administered questions about the 2009 harvest and ensuing sales. I designate these the “2009 households.”Cross-sectional households interviewed from late July 2010 through the end of the survey in March 2011 were administered the exact same set of questions, but with reference to the 2010 harvest season. These are the “2010 households.”Survey questions about the main outcome of interest—crop sales—were asked in a manner that was independent of the interview date. That is, households could indicate the month and year of sales at the crop-plot level. This aspect of the design allows me to treat the 2009 and 2010 households as successive cross-sections generated by random sampling. Figure 2 shows histograms of interview dates for the 2009 and 2010 households.
Notes: Author’s calculations using IHS 3 data. The 12-month IHS 3 cross-sectional survey was carried out over a period of12 months, from March 2010to March 2011. Households interviewed in the early months of the survey could not report their 2010 harvest and sales outcomes because cultivation was ongoing. Instead, they reported farming outcomes from the 2009 season. Interview dates were randomized within districts, at the village level.
I cannot use the panel households in the same way. The research team interviewed all panel households within the span of a few months and asked exclusively about the 2010 harvest and sales. Hence, I drop all panel households from the main analysis. In Section VI.B I will examine trends in education expenditure among panel households, but not in a way that directly exploits the identification strategy used in the main analysis.
Because our main dependent variable is the cumulative value of sales through August of the relevant year, I can only include the 2010 households that were interviewed in September 2010 or later. Thus, the main analysis sample consists of all cross-sectional households below the poverty line that (i) were interviewed about the 2009 harvest or (ii) were interviewed about the 2010 harvest between September 2010 and the end of the survey in March 2011. With the additional sample restriction that the household must be somehow engaged in agriculture, this gives a sample of 3,465 households (779 for 2009 and 2,686 for 2010). When I repeat the analysis with the dependent variable defined as the cumulative value of crop sales through month m, with m varying, I adjust the second part of the sample (interviewed about 2010 harvest) to include only households interviewed in month m+1 or later.
An unfortunate limitation of the IHS 3 is that data on other potentially relevant outcomes were not gathered in a way that can be studied using the same identification strategy. Questions about crop storage, sales of livestock, and sales of other liquid assets were collected with a recall period based on the interview date (for example, “During the last month. “). This leads to incomparable recall periods for households interviewed on different days. This is also a problem for estimates of school costs, which are reported with 12-month recall (I discuss school costs more below), and for data on school enrollment and attendance. Many households were interviewed during school breaks and thus give different information when asked about “current enrollment.”Recall questions about school attendance, covering whether the child was in school in the previous year, and if so, at which grade level, are used to define the number of primary school students in the household, a key independent variable. Total farm output is reported in a wide variety of incomparable units, with many missing conversion factors. Crop sales are one of the only outcomes in the IHS 3 collected with reference to a calendar month and year, presumably because such sales are relatively infrequent, highly salient, and fundamental to livelihoods.
To verify that the survey timing was effectively random, Table 1 shows balance between 2009 and 2010 households for the independent variables used in regressions. Column 3 shows the difference between the group means, with significance stars for t- tests of the difference. The two groups are broadly similar on all of the listed characteristics. The differences in number of males age zero to five and percent of highly educated heads are statistically significant at the 10 percent level, but the magnitudes are too small to be of economic consequence.
Summary Statistics for DID Control Variables, by Year, Poor Households
B. Primary School Expenses
Although primary school fees were abolished after 1994, households still make financial contributions to school operations (see Rose 2002, the primary source for this paragraph, for more details). The most direct form of parent contribution is through the purchase of uniforms, books, notebooks, and other materials. Books and stationery are supposed to be publicly provided, but in practice families often have to supplement whatever is available at the school. Also, each school has a school committee tasked with raising funds for school development projects, such as latrine construction, building maintenance or improvements, or additional payments to teachers. Many school committees do not collect contributions directly from parents. Instead, they enroll the help of village leaders to raise contributions through traditional means, for example, meetings or door-knocking campaigns that may involve implicit or explicit pressure to contribute. Anecdotal evidence suggests that there can be distrust and frustration on both sides. School committee members are disappointed when some parents refuse to make even minor contributions to assist with construction projects. Parents are suspicious that funds are being misappropriated, and they are sometimes confused as to why they are being asked to contribute when school is technically “free.”There can be consequences for nonparticipation. In at least one case, the children of parents who refused to make a contribution equivalent to 4 USD were sent home or not permitted to complete their final exams (Rose 2002).
The education module of the IHS 3 questionnaire collected information on a broad range of school-related expenditures. In this subsection I report summary statistics for these expenditures. Table 2 shows the average annual household-level expenditure per student for various categories of school costs. All rows but the last are based on children enrolled in government primary schools (roughly 90 percent of students). Unfortunately, these estimates are based on 12-month recall, which makes the reference period a function of the interview date. For many households, the 12-month recall covers the beginning of two school years because of the shortened school years, to accommodate the calendar change. Hence, these estimates should be taken as only rough guides to annual school expenses in Malawi.
Per-Student Annual Primary School Expenses (MW Kwacha)
Table 2 shows that a majority of both poor and nonpoor households pay for books, stationery, and uniforms. A substantial portion of households make contributions toward the maintenance or construction of school buildings. A quarter of households make “other”contributions, which may include payments to teachers and school administrators. The average total cost of primary school is substantially lower for poor households than for nonpoor households: 511 MWK (3.52 USD) per child on average for the poor, and 943 MWK (6.50 USD) per child for the nonpoor, though the latter figure is 2827 MWK (19.50 USD) if I include students in private schools. Differences between poor and nonpoor households are apparent on both the extensive and intensive margins: across all categories with 1 percent or more reporting, a greater share of nonpoor households report making payments, and the average payment-among-the-payers is higher for the nonpoor households. It is here that we see clear motivation to move the start of the school year closer to the harvest. The implicit means-testing in Table 2 is driven in part by liquidity constraints. When school begins in January, poor households credibly argue that they lack the funds to make contributions to school, because their liquid resources are committed to planting, which occurs in December and January. In September, the government expects households to have more cash on hand and thus to increase their payments of parent association fees, voluntary contributions, and other expenses.
Contributions by households are important to school operating expenses, even in an atmosphere of technically free education. Official reports indicate that the government spent 3019 MWK per student in 2007, representing 92 percent of primary school costs (Milner, Mulera and Chimuzu 2011). However, I find that households spend 719 MWK per student on average, far greater than the implied 8 percent of costs not covered by the government.10 There are various possible explanations for this discrepancy. The first figure is from 2007, the second from 2010; the survey data may be subject to bias as discussed above; and, it is possible that the 92 percent of costs refers only to teacher salaries and major capital costs, which were contentious issues in the run-up to the 1994 elections that brought about free primary education (Kadzamira and Rose 2003). Nevertheless, even if I make conservative assumptions in interpreting the IHS 3 data on school expenses, it is clear that household payments are fundamental to the operation of the primary school system.
C. Crop Sales
Table 3 shows the distributions of the aggregate number of sales transactions and the total value of sales, by crop, across reporting years. Maize is the crop sold most often, followed by beans. Tobacco represents the biggest share of sales value, followed by maize. However, tobacco is not useful as a means of storing value later into the year. Tobacco is sold exclusively through large auctions administered by a single private firm (Auction Holdings Limited). The auction season typically begins in April and concludes in August or September, soon after the end of the harvest. There is no return to storing tobacco for many months because there is no market for it. Furthermore, although smallholders can and do grow tobacco, the majority of production is from large farms and estates.
Sales Breakdowns by Crop and Year
Figure 3 gives the distribution across crops of the number of transactions and total value of sales, by month. Panel A shows that the tobacco share of sales value falls quickly after August and effectively disappears after October. As a share of total transactions, the three most important crops from August to December are maize, groundnuts, and beans. The decision about when to sell crops during the period most relevant for this paper seems to be focused on these and other food crops.11
Notes: Author’s calculations using IHS 3 data. Panel A shows the monthly shares of total crop sales by sample households in each crop category, over the period June-December. Panel B shows the shares of total sales transactions in each crop category. The data for both panels is pooled across households selling in 2009 and 2010.
V. Results
In this section I present the empirical results. Tests of parallel trends are provided first and then the main findings, including the results using different cutoff months for the measure of the cumulative value of crop sales. The final subsection is for falsification tests.
A. Parallel Trends
The empirical approach of Section III relies on a natural experiment embedded in the IHS 3 cross-sectional survey. With only two years of observations, in 2009 and 2010, I cannot test for parallel trends using just the IHS 3. However, there is scope for assessing parallel trends using the previous survey wave, the IHS 2, collected in 2004–2005.12
In the IHS 2, households did not report the date of crop sales. This makes it impossible to use the same identification strategy that I use in the main analysis. Instead, I adopt a modified approach that has lower power, yet is feasible and represents a valid analysis of pre-trends. Specifically, I combine the 2004 households from the IHS—those reporting crop sales from the 2004 harvest—with the 2009 households from the IHS 3, and estimate triple difference specifications. The dependent variable in these regressions is the total reported value of crop sales through the interview month, and the three dimensions of difference are: (i) the survey year 2004 or 2009, (ii) the number of primary school-aged children in the household, and (iii) the month of interview (from July to January, with June as the excluded month). For the 2004 households the “interview month”is the actual month of interview. These households were quasi-randomly assigned to interview dates from mid-2004 through the first months of 2005. For the 2009 households, all of whom were interviewed in 2010 and provided crop sales details from the year before, I randomly assign households to simulated interview months, in shares equal to those from the 2004 households. I can do this without introducing additional error or assumptions because for these households I observe the full sales history information at the crop–month level. With those data I calculate total sales value up to and including the simulated interview month. I repeat the random assignment of the 2009 households to synthetic survey months 5,000 times and examine the distributions of estimated triple difference coefficients and their standard errors. For this analysis I use only the households below the poverty line, for comparability with the main analysis. With no specific theory about nonparallel trends, I am interested in whether there is any pattern of significant differences during the July–January period.
To summarize the findings of this exercise: I find no indication of nonparallel trends between 2004 and 2009. The distributions of the triple difference coefficients are centered near zero, and the coefficients are far from statistically significant in the overwhelming majority of iterations. Additional information about this procedure, as well as detailed findings, are presented in Online Appendix A.
B. Main Results
Columns 1–3 of Table 4 show the main DID estimates. The dependent variable is the cumulative value of crop sales through August (of either 2009 or 2010). The sample for these regressions includes only households below the poverty line. Column 1 has no control variables beyond those shown, Column 2 adds in the set of household control variables shown in Table 1, and Column 3 adds district effects. The coefficient of interest is on the variable “Num. in primary × 2010,” which corresponds to β3 in Equation 1.
Difference-in-Difference Results
Results in Table 4 show an economically and statistically significant impact of the calendar change on the value of crop sales through August. The estimated effect is stable across specifications, ranging from 1180 to 1301 MWK per child. I treat the Column 3 result, with the full set of controls, as the main result. The significance stars in the table are for two-sided tests. P-values for one-sided tests of the null hypothesis that the coefficient of interest is less than or equal to zero are listed in the bottom panel of the table. In all columns I can reject the one-sided null with 98 percent confidence and the two-sided null with 96 percent confidence.
Estimates of Equation 2, based on the triple difference, are shown in Table 5. The coefficient of interest is the triple interaction term, which is the first one reported, corresponding to β7 in Equation 2. The point estimate is positive in all three columns, consistent with our central hypothesis. Controlling for household characteristics and district effects (Columns 2 and 3) the triple difference coefficient is statistically significant with 91–94 percent confidence. The triple difference results are 1.6–2.2 times the magnitude of the DID results, suggesting that the point estimates for nonpoor households are weakly negative. Overall, the triple difference estimates provide broad support for the DID findings.
Triple Difference Results
In defining the analysis sample, the poverty line is a proxy for access to credit. Other things equal, I expect households below the poverty line to face higher financing costs than those above the poverty line, and hence to rely more on the crop market for short-term liquidity. To examine the robustness of the results to other proxies for credit access, I reestimate the DID and triple difference estimates using various percentiles of the distribution of real consumption-per-capita to define the analysis sample. The results, in Online Appendix D, provide strong support for the findings in Tables 4 and 5.
How does the between-year difference in cumulative sales value evolve in the months following the harvest? To answer that question I reestimate Equation 1 using different months as the cutoff for the construction of the dependent variable. I vary the cutoff month from July to February of the following year. The specifications underlying the third columns of Tables 4 or 5, with the full set of controls, form the basis for these regressions.
Figure 4 shows the coefficient estimates and confidence intervals for the coefficient of interest for each cutoff month. Each month-specific coefficient is from a separate regression. The left panel is for the double difference; the right panel is for the triple difference. The change over time aligns with exactly what we expect to see if the effects are driven by the school calendar change and if most school costs are incurred in the first couple months of the year. On the left, the magnitude and statistical significance of the point estimate for poor households is stable through November, then falls by December when households in 2009 sell crops in anticipation of the start of school. The point estimate is positive but no longer statistically different from zero in December and January. By February, the point estimate turns negative. This negative effect, though imprecisely estimated, has a clear interpretation. In 2009, households with primary school children completed their crop sales within the first one to two months of the school year (that is, by February) and enjoyed the gains from delaying some sales until crop prices increase. The effect is only suggestive, but it provides support for the idea that early selling eventually leads to a net reduction in cumulative sales revenue.
Notes: Author’s calculations from IHS 3 data. Dots represent point estimates, horizontal bars represent 90 percent confidence intervals. The left panel shows DID coefficient from regressions based on Specification 1. The right panel shows triple difference coefficients from regressions based on Specification 2. The dependent variable for each coefficient is the cumulative value of crop sales through the listed month. Sample sizes at left (reading from July to February) are 3549, 3465, 3295, 2918, 2314, 2002,1529, and 1141. Samples sizes atrightare 7060, 6861, 6467, 5686, 4588, 4014, 3045, 2285. Full results in the Online Appendix.
The right panel of Figure 4 shows a similar time path for the triple difference coefficients. The triple difference coefficient for August is the only one that is statistically different from zero. The magnitudes of the point estimates decay more gradually as the months progress than do those from the DID. Yet, the overall pattern from both figures is consistent with the hypothesis that the calendar change increased pre-September sales by poor households with primary school age children, and in the long run reduced the total value of crop sales by these households.
C. Falsification Tests
In 2016–2017 the Malawi National Statistical Office collected the fourth round of the IHS (the IHS 4), using a design similar to that of the IHS 3. The surveyed households were quasi-randomly assigned to interview dates, and hence to reporting sales after either the 2015 or 2016 harvests, generating the same experimental conditions exploited in the main analysis. However, there was no school calendar change in 2016–2017. The IHS 4, then, is the ideal setting for a falsification test.
I use the poor households from the IHS 4 to estimate regressions similar to those in Column 3 of Table 4, with the full set of controls, for each month from July to February. I then repeat this analysis after transforming the dependent variable using the inverse hyperbolic sine. In all cases, the coefficients are small in magnitude and far from statistically significant. There is no evidence that the sales pattern from 2009–2010 is repeated in 2015–2016. This further supports the causal interpretation of the main results: the school calendar change induced earlier sales. Additional details about this falsification exercise are provided in Online Appendix E.
VI. Discussion and Extensions
The analysis presented in the previous section shows that the 2010 school calendar change induced poor households to sell crops earlier than they would have otherwise, with the amount increasing per primary school-aged child. With identification based on a difference-in-difference that controls for interannual differences within poor households and within households that have children, I interpret this effect as causal. The causal interpretation is further supported by the similarity between the estimated effect and the cost of school attendance. The preferred DID estimate is a 1271 MWK increase in crop sales per child; the average per-child cost of primary school is 719 MWK in public school and 1,657 MWK across all schools (Table 2).
In this concluding section I consider three extensions to the analysis. The first is to estimate the welfare costs from financing school expenditures through crop markets. The second is to examine trends in schooling-related outcomes after the calendar change. The third is to explore whether the substantial increase in early season sales in 2010 may have affected crop prices.
A. Estimating Forgone Sales Revenue
What do households give up by selling early? To answer this question I need to estimate the expected change in crop prices from August to December. Using the time series of market price data for maize, rice, and beans from the Ministry of Agriculture (the same data used for Figure 1), I employ two approaches to estimation. First, using weights reflective of the relative importance of each of these three crops in total sales value, I calculate the average percent change from August to December over the 11 years of maize data and four years of rice and beans data that pre-date the 2010 policy change, and then take the weighted average of those percent changes.13 This returns an expected increase of 26.5 percent. Second, I repeat the procedure, but instead of taking the simple average of the August–December change, I assume that farmers have adaptive expectations with decay parameter λ ∈ {0.25, 0.5}, and then take the weighted average across crops. With this approach, the expected increase is 17.3–20.1 percent. Note that because the percentage markups each year are calculated relative to that year’s June price, variation in within-year supply and demand conditions, as well as long-term trends and inflation, are largely accounted for.
With the range 17.1–26.5 percent as the expected return to delaying crop sales until the end of the year, average forgone revenue per child ranges from 1271 × 0.171 = 217 MWK ($1.50), using the DID estimate, to 2357 × 0.265 = 625 MWK ($4.31), using the triple difference estimate. The range 217–625 MWK includes 511 MWK, the average cost of school for poor households (from Table 2), and represents 30–87 percent of the average cost of school across all households. To the average poor household, the calendar change introduced an additional, indirect cost of school roughly equivalent to the direct cost.
Households’ willingness to pay what is effectively an annual interest rate in the range of 69–106 percent to finance school costs may be partly due to the nationwide, covariant nature of the expenditure shock. If the change in expense timing were idiosyncratic, affected households may have borrowed to finance expenditures at rates better than the implied expected quarterly interest charged by the crop market. But when the entire country is impacted at once, the financial fragility of poor households is revealed through their reliance on crop sales to finance even a relatively small outlay.
One concern about these welfare estimates is that they are based on market prices, not the farmgate prices that are most relevant for farmers. However, for the one crop that has sufficient representation in the IHS 3 data to construct a time series of farmgate prices— maize—I see an intra-annual pattern similar to that of the market price data.14 The average August–December increase in the reported farmgate price of a 50-kg bag of maize, the most common unit of sale, is 28 percent in the household survey data for 2009 (see Section VI.C for a discussion of the differences between 2009 and 2010). In this case the similarity between farmgate prices and average market prices is not surprising. The two are related by arbitrage conditions, and the Ministry of Agriculture data cover a large number of maize markets for a relatively small country.15
Another potential concern is that these welfare calculations do not allow for depreciation during storage. If a substantial portion of grain stored from August–December is lost to spoilage, pests, or theft, then our estimates of forgone revenue are too high.16 However, the most recent empirical evidence indicates that storage losses of cereals and dry legumes are well below 5 percent in much of sub-Saharan Africa. This is in contrast to the estimates of 20–40 percent that are sometimes quoted in the policy literature.17 The discrepancy stems from our narrower interest in the depreciation that occurs during home storage by producers. In a careful study from Ghana, researchers estimate that maize losses from the field to the point-of-sale are equal to 18.25 percent of production (and further losses would then be incurred through food waste by consumers). Yet only 1.25 percent of crop loss occurs during home storage by farmers. The remainder occurs during harvesting (5.59 percent), processing (2.97 percent), transport to home (2.66 percent), loading on vehicles (1.69 percent), and at other points in the supply chain (University of Ghana 2008, as cited in Zorya et al. 2011). Even more relevant for our setting, Kaminski and Christiaensen (2014) use farmer reports of post-harvest losses from the IHS 3 data to estimate average household-level post-harvest losses for farmers in Malawi. They find that farmers lose an average of 2.9 percent of harvest over 11 months of potential storage, or roughly a quarter of a percent per month. The highest figure I could find for depreciation of cereals in sub-Saharan Africa during post-harvest storage was 8 percent, in a recent FAO report (Gustavsson et al. 2011).
The relevant takeaway from these findings is that allowing for possible storage losses over three to four months does not substantially reduce the 17.1–28 percent expected return to selling crops later. The Kaminski and Christiaensen (2014) estimate, based on the same nationally representative data set used in this paper, suggests that I should adjust the estimated returns by only a fraction of a percent. Even if I take the upper bound estimate of 8 percent from the FAO and attribute it entirely to the August–December period, the expected quarterly return from the farmgate prices is still 20 percent, equivalent to an annualized cost of finance of more than 80 percent.
B. Changes in School-Related Outcomes
I have shown that the calendar change imposed a substantial, indirect cost on many poor households. It is possible that the change also created some schooling-related benefits. Increased parent contributions may have led to improvements in school quality. The program may have increased enrollment, either directly, by making it easier for households that previously had difficulty saving for school to pay school-related expenses, or indirectly, if improvements in school quality raised the opportunity cost of dropping out. A direct, positive effect on enrollment would only occur if children were previously denied admission because of nonpayment of school expenses. Despite pressure to contribute to the local schools and buy supplies, such denials were technically illegal, and there is no evidence that they were common (Kadzamira and Rose 2003; Behrman 2015). The calendar change could also decrease enrollment, if the negative wealth effect from selling early pushed marginal households to substitute child labor for schooling.
The calendar change affected all schools simultaneously, so there is no clean experimental design for testing whether it led to improvements in schooling outcomes. However, I can examine trends in school quality and attendance on either side of the reform. For this I employ three data sources not used above. The first is the survey of community leaders conducted during the IHS 3, in 2010–2011, and the followup Integrated Household Panel Survey (IHPS), in 2013. These surveys cover numerous topics about the local community, including details about the nearest government school. The second are the panel household surveys from the IHS 3 and IHPS, which were excluded from the analysis in Section V.18 In the panel I can examine whether schooling payments by poor and nonpoor households exhibit different trends after 2010. Finally, I use the 2004, 2011, and 2015–2016 Demographic and Health Surveys (DHS) for Malawi to examine trends in school attendance and literacy of household members over the age of 15. See Online Appendix F for more details about the community surveys and DHS data.
Panels A and B of Table 6 report schooling characteristics from the community surveys. The mean numbers of teachers and students increased at roughly the same rate from 2010 to 2013 (18.4 percent and 16.4 percent), but the net increase in teachers was concentrated in schools with higher student-to-teacher ratios, leading to a reduction of 22.6 students per teacher on average (a 20.3 percent decrease). This apparent improvement in average school quality contrasts with an increase on both the intensive and extensive margins in the number of classes being taught in nonpermanent structures, possibly due to physical deterioration of existing buildings or to increases in attendance that were not accompanied by new construction. In Panel B there is suggestive evidence of a small reduction in the number of students covered by school nutrition programs, though I cannot be certain about the sign of the change because of the categorical nature of the data.
Changes in School Quality and Schooling Expenditures, from IHS 3 and IHPS
Panel C of Table 6 shows the trends in per-child school expenditure by the panel households. From 2010 to 2013, nominal per-child education outlays by poor households grew by 119 percent, while those by nonpoor households grew by 78 percent. Much of the growth for the nonpoor is due to inflation, which was 64 percent from July 2010 to July 2013.19 These trends are consistent with the interpretation that the move to a September start date induced much faster growth in school payments by poor households than by nonpoor households. The government appears to have accomplished its objective to increase the capacity of poor farming households to pay school costs by moving the start of school closer to the harvest.
Table 7 reports the trends in net attendance ratio (NAR) and demonstrated literacy from the Malawi DHS (National Statistical Office 2005, 2011, 2017). The NAR is the total proportion of the primary school-aged population, defined as age 6–13 for Malawi, that is enrolled in school. From 2010 to 2015 there were noticeable increases in NAR for boys, girls, and children in rural households. Yet, across all four subgroups, the average annual growth rate in NAR from 2004 to 2010 was higher than that from 2010 to 2015. In the lower panel I report the percentage of primary school graduates who can read none, part, or all of a sentence presented by an enumerator. This direct measure of literacy is a proxy for education quality. I restrict attention to young adults aged 15–16 because the 2015–2016 cohort in this age range would have enjoyed multiple years in primary school after the 2010 reform. The overall trend is one of gradual improvements in literacy, with some exceptions. After 2010, girls showed improvement across the distribution, while boys experienced a drop in full literacy (as measured by the ability to read the entire sentence).
School Attendance and Literacy in the Malawi DHS
Overall, the trends in school quality in the post-calendar-change period are mixed, at best. If the calendar change caused improvements in school-related outcomes, the patterns in Tables 6 and 7 would only arise if the counterfactual trends (without the calendar change) were broadly negative. Hence, while we cannot rule out that changing the timing of the school year made schooling better, there is little suggestive evidence that it did.
C. Did Early Sales Affect Crop Prices?
In the aggregate, earlier sales by poor households represent an increase in the supply of crops in the market during the first months after harvest. This section explores whether there is any discernible effect on crop prices in 2010 that can be attributed to these early sales.
Remarkably, 2010 did turn out to be an outlier in the intra-annual price dynamics for one crop: maize. The other crops for which I have time series data, rice and beans, exhibit the normal price cycling. In 2010, the average increase in maize prices from August to December at Malawi markets was essentially zero. The left panel of Figure 5 shows the 2010 time path relative to other years, using market price data from the Ministry of Agriculture. The solid lines show the maximum and minimum price changes of all years excluding 2010 (the outer envelope). The dashed line running horizontally at zero is the time path in 2010. A similar pattern is evident in farmgate maize prices. The right panel of Figure 5 shows a comparison between farmgate prices in 2009 and 2010, by month, from the IHS 3 data. The solid line, representing 2009, closely matches the price path from other years. The dashed line is 2010. Farmgate prices, like market prices, show no price cycle through December.
Notes: PanelAshows author’s calculations from Ministry of Agriculture price data. Panel B shows author’s calculations from IHS 3 data. Panel B shows the price for a 50-kg bag, the most common unit of sale, and the only unit for which there are sufficient observations not aggregated across multiple sales to construct a time series through December.
This anomaly raises two questions. The first is in regard to the welfare effects estimated in Section VI.A. I opted not to adjust for this unexpected lack of a 2010 maize price cycle when calculating the opportunity cost of selling early. I made this decision because households are unlikely to have anticipated the lack of a price cycle for maize, and poor households surely would not have anticipated it differentially based on their numbers of primary school children. Also, while maize is the most important single crop in terms of sales value, other crops are equally important in the aggregate (see Figure 3), and those for which I have data exhibited the normal price cycle in 2010.
The second question relates to whether the lack of a price cycle could be endogenous to the school calendar change. It is not ex ante obvious that increasing the volume of marketed maize early in the season should dampen the price cycle. If it were to do so, the likely mechanism would be through shifting storage from farmers, who store grains for speculation, savings, and future consumption, to traders, who are engaged in a mix of inter- spatial and inter-temporal arbitrage. A full accounting of these and other relevant forces is beyond the scope of this paper.
However, despite this intriguing anomaly, I think it is unlikely that maize price dynamics in 2010 were endogenous to the calendar change. Other crops did not show unusual price cycles in 2010. Furthermore, the maize price cycle returned to its historical norm in 2011 and 2012, even though primary school again began in September. The August–December price increase was well over the 25 percent historical average in 2011, and slightly below 25 percent in 2012. Hence, the unexpected behavior of maize prices in 2010 is likely a function of forces unrelated to this paper. Further exploration is left to future work.
VI. Conclusion
The results of this study provide strong empirical support for the hypothesis that credit-constrained households are forced to “sell low”to accommodate immediate needs. The findings are based on a natural experiment related to the timing of school-related expenses. Everything about the setting suggests that the effects are causal. What, then, are the suggestions for policymakers? The lessons for policy are not limited to the timing of school fees, although the results do suggest that allowing flexible timing of school-related payments could be beneficial for poor households, if such a policy were easily implementable. Indeed, policymakers seeking to use the insights of behavioral economics to alter household consumption and investment portfolios would do well to differentiate between optional commitment devices and large-scale changes that force households to spend more money closer to the harvest.
The broader lesson of this paper is that weak financial markets and highly seasonal crop prices combine to be especially detrimental for poor households. All commitment devices have opportunity costs. Yet the real opportunity costs of timing changes that encourage investment are especially high for poor agricultural households that use crop markets for liquidity. Access to inexpensive credit would allow these households to finance their school expenditures at lower rates than those afforded by crop markets. Alternatively, better development of crop markets to dampen the severity of intra-annual price cycles would lower the penalty for selling early. In the absence of such changes, it is likely that both predictable and unpredictable expenditures will continue to force poor households to sell crops at prices well below those received by their wealthier counterparts, further deepening existing inequalities.
Footnotes
For helpful comments and discussions the author thanks Jenny Aker, Harold Alderman, Chris Barrett, Lorenzo Casaburi, Esther Duflo, Pascaline Dupas, Andrew Foster, John Friedman, Supreet Kaur, Katrina Kosec, David Levine, Mark Long, Travis Lybbert, Jeremy Magruder, Will Masters, Dawit Mekonnen, Ted Miguel, James Mwera, Lokendra Phadera, Dan Posner, Imran Rasul, Jon Robinson, Betty Sadoulet, Jack Willis, two African Development Bank readers, two anonymous referees, and seminar participants at NEUDC, the CEGA R2 research retreat, IFPRI, the Midwest Development Conference, Montana State, UC San Diego, and the University of Washington. Any errors are the responsibility of the author. The African Development Bank provided funds to support this work. The author has no disclosures or conflicts of interest. Replication code and instructions for accessing the data for this paper are available at https://doi.org/10.6077/xp44-tf07
↵1. This approach is conservative in that if the timing of school payments was fully flexible, the school calendar change would have no impact on the timing of crop sales. Nonetheless, it would be useful for future work to examine how the timing of payments relates to the timing of the school year.
↵2. Currently, the school year begins in January in Botswana, Mozambique, South Africa, Zambia, and Zimbabwe.
↵3. This change affected both primary schools and secondary schools. I focus on primary schools for a number of reasons: 93 percent of students in the data are primary school students, secondary school is not free and has a very different cost and payment structure, and secondary school enrollment is especially low for the households in poverty that constitute the main sample.
↵4. This point is from personal communication with James Mwera, Invest in Knowledge Malawi, August 2016.
↵5. As a practical matter, the regressions span only two years and include time fixed effects, so there is no consequence to using nominal or real prices.
↵6. The coefficients of interest will also turn out to be statistically significant using two-tailed tests.
↵7. I use the IHS 2 survey, collected in 2004–2005, in tests of parallel trends. See Section V.A and Online Appendix A for details. I use the IHS 4 survey, from 2016–2017, to implement falsification tests, as described in Section V.C and Online Appendix E. The IHS 2 and IHS 4 surveys are similar in design to the IHS 3, with some important exceptions described below.
↵8. Details about survey design and sampling strategy were drawn from National Statistical Office (2012).
↵9. The three largest cities, Blantyre, Lilongwe, and Zomba, were divided into rural and urban areas, so that the sample effectively contains 31 districts. Also, for the two Lilongwe districts, 36 enumeration areas were selected for surveying, to reflect the large population of the city.
↵10. If 3019 MWK per student covers 92 percent of costs, then the remainder is 3019 × (0.08) = 263 MWK.
↵11. More information about the timing of other expenditures could be helpful in future research, for comparing the relative importance of immediate cash needs and school-related payments.
↵12. The IHS 1, from 1998–1999, differs in too many ways to be useful. See the discussion in Online Appendix A.
↵13. Those weights are 0.472 for maize, 0.281 for beans, and 0.247 for rice.
↵14. The challenge in assembling time series for other crops is that sales are reported in a large number of different units, with many missing unit conversion factors. Also, some respondents reported the total quantity and total volume aggregated across multiple sales, which are not helpful for constructing time series of prices. Maize is the only crop for which a single unit, the 50-kg bag, occurs frequently enough in reports of single sales to allow me to estimate average prices through December.
↵15. Despite frequent assumptions to the contrary, a recent review of the evidence suggests that the crop trading sector in sub-Saharan Africa is generally competitive at the local level, with traders passing on market price changes to farmers. See Dillon and Dambro (2017).
↵16. Relatedly, if storage involves substantial labor or materials costs, the returns to intertemporal arbitrage are lower than estimated. I think it likely that storage costs do reduce the profitability of storage, but only to a small extent. In a recent study with cowpea farmers in Niger, where potential depreciation during storage is substantial, the maximum average district-level expenditure on storage technologies represents only 3 percent of estimated harvest value (Aker and Dillon 2018). This is likely an upper bound on storage costs in Malawi. Also, any fixed costs of storage are invariant to intensive margin adjustments in the timing of crop sales.
↵17. See Kaminski and Christiaensen (2014) and Affognon et al. (2015) for discussions of the origins and persistence of stylized facts about post-harvest losses in the academic and policy literatures.
↵18. Recall from Section IV.A that I cannot use the panel data to test the central hypothesis about the timing of crop sales because most panel households were interviewed in July–September, so I do not observe variation in sales between September and December.
↵19. Inflation figure is from the IMF International Financial Statistics database: http://data.imf.org (accessed February 11, 2021).
- Received June 2017.
- Accepted September 2019.
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