Malaria Eradication in the Americas: A Retrospective Analysis of Childhood Exposure^*

2.2 Efforts against Malaria in the Southern US, circa 1920

The turn of the 20th century saw considerable advances in the scientific understanding of the disease. Dr. Charles Louis Alphonse Laveran, of the French army, showed in the early 1890s through microscopic studies that malaria is caused by a single-celled organism. Dr. Ronald Ross, of the British Indian Medical Service, discovered in the late 1890s that malaria is transmitted via mosquitoes. These discoveries proved invaluable to addressing the malaria problem in a scientific and systematic way, and both men later won Nobel Prizes for Medicine. But a workable package of techniques for malaria control was still a ways off.

The US government’s interest in vector-borne diseases arose in the 20th century, not because of a new-found interest in the Southern region, but because of its involvement in Cuba and in the Panama Canal Zone. Early in the occupation of Cuba, the US Army dispatched a team of physicians, among them Dr. Walter Reed, to Havana to combat yellow fever and malaria. Armed with the new knowledge about these diseases (from Laveran, Ross, and others), the Army was able to bring these diseases under control in that city. Another team of American physicians, this time led by Dr. William Gorgas, was able to bring these diseases under control in the Canal Zone, which was a considerable challenge given that much of the area was a humid, tropical jungle.

The knowledge generated by US Army doctors on malaria control in Cuba and Panama inspired work back home in the South in the latter half of the 1910s. Several physicians in the United States Public Health Service (PHS) began collecting information on the distribution of malaria throughout the South and the prevalence of the various species of parasites and mosquitoes.² The PHS began actual treatment campaigns in a limited way, first by controlling malaria in a handful of mill villages. The Rockefeller Foundation, having mounted a successful campaign against hookworm in the early 1910s, also funded anti-malarial work later in the decade through its International Health Board (IHB). These two groups sponsored demonstration projects in a number of small, rural towns across the South. They employed a variety of new methods (spraying of larvacides, water management, window screening, and mass administration of quinine) and most of these demonstrations were highly successful, resulting in 70% declines in morbidity (i.e., sickness that does not result in mortality).

The federal government’s large-scale efforts against malaria in the South began with World War I (WWI). In previous wars, a significant portion of the troops were made unfit for service because of disease contracted in or around encampments. The PHS, working now with both a strong knowledge base on malaria control and greatly increased funding, undertook drainage and larviciding operations in Southern military camps as well as in surrounding areas. After the War, the IHB and PHS expanded the demonstration work further. By the mid-1920s, the boards of health of each state, following the IHB/PHS model, had taken up the mantle of the malaria control in all but the most peripheral areas of the region (Williams, 1951). The South experienced a drop in malaria mortality of more than 60 percent in the decade of the 1920s.

2.3 The Worldwide Campaign to Eradicate Malaria, circa 1950

While some of the innovations in malaria control diffused to less-developed regions, the tropical countries of the Americas would wait for further technological advance before launching serious campaigns against malaria.³ These campaigns had a peculiar starting point: In 1941, a Swiss chemist seeking to build a better mothball re-discovered a chemical known today as DDT (short for dichloro-dipenyl-trichloro-ethane). Early tests showed this new chemical to be of extraordinary value as a pesticide: it rapidly killed a variety of insects and had no immediately apparent effects on mammals. DDT proved enormously valuable to the Allied war and occupation efforts in combating typhus and later malaria.⁴ The United Nations Reconstruction and Relief Agency used DDT in the late 1940s to essentially eradicate malaria from Sardinia in the lapse of a few years.

The World Health Organization (WHO) proposed in the early 1950s a worldwide campaign to eradicate malaria. While the WHO mostly provided technical assistance and moral suasion, substantial funding came from USAID and UNICEF. The nations of Latin America took up this task in the 1950s. While individual nations had formal control of the design and implementation of the programs, their activities were comparatively homogeneous as per the dictates of their international funders. The central component of these programs was the spraying of DDT, principally in the walls of houses. Its purpose was not to kill every mosquito in the land, but rather to interrupt the transmission of malaria for long enough that the existing stock of parasites would die out. After that, the campaigns would go into a maintenance phase in which imported cases of malaria were to be managed medically.

The Latin American countries analyzed in the present study (Mexico, Colombia, and Brazil)⁵ all mounted malaria eradication campaigns, and all saw large declines in malaria prevalence. Panel A of Figure 1 shows malaria cases per capita in Colombia. (Comparable time-series data were not available for the other four countries. Nevertheless, there is little doubt that malaria declined in all four countries immediately following these campaigns.) A decline of approximately 80 percent is seen in the graph. Throughout Latin America, the campaign ultimately proved inadequate to the task, and, in many areas, malaria partially resurged two decades later. But in almost all parts of the hemisphere, malaria never returned to its levels from before the application of DDT.

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Figure 1

Malaria Incidence Before and After the Eradication Campaign, Colombia

Notes: Panel A reports time-series data on notified cases of malaria for Colombia (SEM, 1979) for various years. Panel B shows the post-campaign decline in malaria mortality versus pre-campaign levels across Colombian departmentos. The y axis displays the estimated decrease in malaria mortality post-intervention. The x axis is the pre-campaign malaria mortality rate. (The 45-degree line represents complete eradication.) All variables are expressed per 100K population. SEM (1957) and the Colombian Anuario de Salubridad (DANE, 1968–70) are the sources for the departamento data. The malaria-eradication campaign in Colombia (like Mexico and Brazil) started mass spraying around 1957. (The time-series data required for this figure were not available in comparable form for the other three countries.)

2.4 Research Design

The first factor in the research design is that the commencement of eradication was substantially due to factors external to the affected regions. The eradication campaign relied heavily upon critical innovations to knowledge from outside the affected areas. Such innovations were not related to or somehow in anticipation of the future growth prospects of the affected areas, and therefore should not be thought of as endogenous in this context. This contrasts with explanations that might have potentially troublesome endogeneity problems, such as, for example, positive income shocks in the endemic regions.

Second, the anti-malaria campaigns achieved considerable progress against the disease in less than a decade. This is a sudden change on historical time scales, especially when compared with trend changes in mortality throughout recent history, or relative to the gradual recession of malaria in the midwestern US or Northern Europe. Moreover, I examine outcomes over a time span of 60 to 150 years of birth, which is unquestionably long relative to the malaria eradication campaigns.

An additional element in the identification strategy is that different areas within each country had distinct incidences of malaria. In general terms, this meant that the residents of the US South, southern Mexico, northern Brazil, and the tierra caliente of Colombia were relatively vulnerable to infection.⁶ Populations in areas with high (pre-existing) infection rates were in a position to benefit from the new treatments, whereas areas with low endemicity were not. This cross-regional difference permits a treatment/control estimation strategy.

The advent of the eradication effort combines with the cross-area differences in pre-treatment malaria rates to form the research design. The variable of interest is the pre-eradication malaria intensity. By comparing the cross-cohort evolution of outcomes (e.g., adult income) across areas with distinct infection rates, one can assess the contribution of the eradication campaigns to the observed changes. (Specific estimating equations are presented below.)

How realistic is the assumption that areas with high infection rates benefited more from the eradication campaign? Mortality and morbidity data indicate drops of 50 to 80 percent in the decade after the advent of the eradication efforts. Such a dramatic drop in the region’s average infection rate, barring a drastic reversal in the pattern of malaria incidence across the region, would have had the hypothesized effect of reducing infection rates more in highly infected areas than in areas with moderate infection rates. Data on malaria cases by Colombian departaments allow us to examine this directly: the decline in malaria incidence as a function of intensity prior to the eradication campaign is found in Panel B of Figure 1. The basic assumption of the present study — that areas where malaria was highly endemic saw a greater drop in infection than areas with low infection rates — is borne out. (Similar results are seen for US and Mexican states; data for Brazilian states were not available.)

Finally, the timing of the eradication campaign should induce variation in childhood malaria infection that has a marked pattern across year-of-birth cohorts. The present study considers the effects of childhood malaria infection on later-life outcomes, so it is useful to characterize childhood exposure to an eradication campaign. This is shown in Figure 2. Consider a campaign that starts in year zero and takes effect instantaneously. Cohorts born after this date will be exposed to the campaign for their entire childhood. On the other hand, those cohorts who were already adults in year zero will have no childhood exposure to the campaign, while the ‘in between’ cohorts will be partially exposed during childhood, as shown in the figure. I exploit this timing in two ways. First, in Section 4, I compare the ‘born after’ cohorts to the ‘already adult’ cohorts by taking differences across these cohort groups. Second, in Section 5, I use the functional form of childhood exposure in estimation using data for all cohorts. (I discuss some alternative functional forms in Section 6.2.)

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Figure 2

Childhood Exposure to Eradication Campaign

Notes: This graph displays on the fraction of childhood that is exposed to a hypothetical (and instantaneous) campaign as a function of year of birth minus the start year of the campaign.

These four factors (the external origin of the campaigns, the quick reduction of malaria that followed, the use of nonmalarious areas for comparison, and the differential incidence of eradication benefits across cohorts) combine to form the research design of the present study.

4.1 United States

Areas in the US with higher malaria burdens prior to the eradication efforts saw larger cross-cohort growth rates in income, as measured by the occupational proxies. These results are found in Table 1. The first row of Panel A contain estimates for the basic specification of equation 1, which includes a dummy for being born in the South plus the natural logarithm of state unskilled wages in 1899. The former variable allows for differential income shifts across regions, while the latter variable, drawn from Lebergott (1964), serves as a correction for possible mean reversion in income. If the oldest cohorts had high malaria infection and low productivity because of some mean-reverting shock, we might expect income gains for the subsequent cohorts even in the absence of a direct effect of malaria eradication on productivity. I present results for both income proxies available for the US: the occupational income score and the Duncan socioeconomic indicator. The first two columns of the table report results using the measure of 1890 malaria mortality, while the remaining two columns use an alternative measure of malaria intensity: a malaria-ecology variable due to Hong (2007).

The estimates for malaria are not substantially affected by the inclusion of a number of additional control variables. The balance of Table 1, Panel A contains these results. The second row controls for additional state-of-birth-level measures of health, including fertility and infant mortality in 1890; late-1910s hookworm infection; state public-health spending and the number of doctors per capita in 1898; and the fraction of recruits rejected from service for health reasons by WWI-era Army physicians. The third row of Panel A shows the estimated effect of malaria when controlling for several education-related controls: the 1910 adult literacy rate, and the logarithmic change (circa 1902–32) of teacher salaries, pupil/teacher ratios. The fourth row, marked “Other”, includes a mixed basket of controls: male unemployment rates from 1930, the 1910 fraction black, and the 1910 fraction living in urban areas. The specification employed in the final row includes all of the above control variables simultaneously in the regression. Relatedly, the upper left graph in Figure 3 displays a scatter plot of the orthogonal component of cross-cohort income growth versus malaria (the 1890 measure), after having projected each variable onto the broad set of state-level controls.

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Figure 3

Cross-Cohort Differences in Income versus Malaria

Notes: Each panel plots the cross-cohort change in income versus malaria for the four countries studied. The y-axes are the changes in the indicated income proxy from cohorts born well before the campaign (before 1895 in the U.S., and before 1940 in Brazil, Colombia, and Mexico) to cohorts born after the campaign (after 1920 in the U.S., and after 1957 elsewhere). The x-axis plots the malaria proxy for each country. Appendices A and B describe, respectively, the outcome variables and the malaria measure. Both variables are residuals from having projected the original data onto the controls from the “full controls” specification in the text and Appendix C. The dashed line is the best-fit regression line. State labels are left-justified on the corresponding coordinates.

If these noisy proxies of malaria are measured with independent errors, then the measurement-error bias in any one can be corrected by using the other malaria variable as an instrument. Indeed, as seen in first row of Panel B, the instrumented (2SLS) estimate is higher than the OLS estimate in almost every case. Furthermore, similar results (shown in the second row of the same panel) are obtained using state-average temperature and altitude (plus the interaction of the two) as instruments. The assumption of independence of errors might seem inappropriate for the climate-related instruments, but similar results are obtained by using various subsets of the instruments, and accordingly, a Hausman/NR² test fails to reject the null of identical parameter estimates in the second stage.

These results are most likely not because of migration. First, recall that the malaria variable is, throughout all of the main analysis, assigned by area of birth, never by area of residence. This rules out the mechanism that high-income workers migrate to areas where malaria was controlled. Second, I obtain similar results with two additional checks for migration confounds. These results, estimated using the “full controls” specification from Panel A, are seen in Panel C of Table 1. The first two rows decompose the results by residence in one’s state of birth. To compute these estimates, I construct two cohort-level datasets, one for movers and another for nonmovers. Significant and positive effects on income are seen for those who reside in their state of birth (“nonmovers”) and those who reside in a different state (“movers”). I then re-do the analysis using the state of birth of the individual’s father (results for mother’s birthplace are similar). Results suggest an effect of childhood exposure to malaria on income, but data availability places certain limitations on this approach. Namely, parental state of birth is not available for people in the sample born after 1915, so this requires me to redefine the treatment group to those with only partial childhood exposure to the campaign (born 1905–1915 in this case). Standard errors are therefore larger, in accordance with the narrower span of cohorts employed. In the third row of Panel C, I re-estimate the model above, but restrict the sample to those with data on parents’ birthplace. The coefficients for this model are broadly similar to those above, although larger in some cases and smaller in others. Next, I consider results for just those individuals with native-born fathers. I use the redefined treatment group, but otherwise replicate the specification from above in that the malaria variable is based on one’s own state of birth. Finally, I assign malaria based on father’s state of birth, and repeat the analysis. These estimates, found in the fifth row of Panel C, are similar to their baseline estimates in the third and fourth rows.

Finally, results are similar across broadly defined regions, but more precisely determined when considering the Southern and border regions. These estimates are found in Panel D of Table 1. The first row replicates the “full controls” specification from above for the Southern states and states that border the South. Estimates are similar to those above, and statistically significant in 3 of the 4 columns. The second row of Panel D uses the remaining states to estimate the same equation. The coefficients are similar to those above, although imprecisely determined. This latter result is perhaps not surprising given that the malaria problem was largely concentrated in the Southern region of the country.

These point estimates imply substantial, but not unreasonable, reduced-form magnitudes for the effect of childhood exposure to malaria. The income variables are in natural logarithms, so the exposure coefficients can be interpreted approximately as percentage changes in income per unit increase in the independent variable. Recall that the malaria measure is renormalized by the difference across the 95th and 5th percentile states.⁹ Therefore, these point estimates suggest a reduced-form effect on income of ten to fifteen percent when comparing the non-malarious to the highly malarious states. That is, in the states with high levels of malaria, cohorts born after the anti-malaria campaign earned 10–20% more than the previous generation, relative to the benchmark of cohorts in malaria-free states.

5.1 Pooled Regression Analysis

Statistical tests indicate that the shift in the income/pre-campaign-malaria relationship coincided with exposure to malaria eradication, rather than with certain trends across cohort or time. These tests are performed using the three-dimensional cohort/panel data structured by year of birth, census year, and area of birth, the construction of which is described in Section 3 and Appendix A. The following equation is estimated:

in which Exp_k is potential exposure to the malaria-eradication campaign (defined above), M_j is the pre-campaign malaria intensity in area of birth j, the xji are area-of-birth controls, and the δ_k, δ_t, and δ_j are fixed effects for year of birth, census year, and area of birth, respectively. (The main effects of the area-of-birth and exposure controls are therefore absorbed by these fixed effects.)

Table 4 reports estimates of equation 2 under a variety of specification assumptions. The dependent variables and countries are indicated in the Panel headings. The Table reports present estimates of β, the effect of childhood exposure to the campaign. The controls (the xji) used for first three columns comprise region and mena-reversion controls, which corresponds to the “basic” specification in Section 4. The last three columns uses variables in the “full controls” specifications above.

Panel A of Table 4 contains estimates for the United States. The outcome variable is each cohorts average (log) occupational income score. Estimates most comparable to those in Section 4 are found in columns (1) and (4) of the row labeled “Baseline”. The magnitudes here are similar to those estimated using long differences across cohorts, which should be the case. (These two types of estimates will not be exactly the same because partially exposed cohorts are now included in the sample.) The remaining columns of the baseline row present specifications that also include birthplace-specific trends across cohorts, with the trend being modeled as either a first- and second-order polynomial trend in year of birth. Estimates on childhood malaria exposure are not sensitive to controlling for these smooth trend across cohorts.

The rest of Table 4, Panel A considers the issue of childhood exposure versus contemporaneous exposure to malaria. If the effect on income were truly via contemporaneous exposure, this might appear as a cohort effect in that those born earlier spend a larger fraction of their working lives exposed to malaria. (Note that the estimates from the literature suggest relatively small effects on output of episodes of malarial fever, although persistent morbidity would also depress labor productivity contemporaneously.) The first attempt to address this confound is seen in the second row of Panel A. This specification maintains the assumption that areas had similar time trends prior to the eradication campaign, but allows for birthplace-specific trend and level shift after 1920. The estimates on childhood exposure tend to be a bit lower here, although they rise as I also control for differential trends across cohorts as well. The next row allows instead for effects of birthplace×time effects, which relaxes the previous assumption that pre-campaign time trends were the same across areas. In the fourth row of Panel A, I instead drop all of the census years taken prior to 1930, which, by drawing observations from after the campaign, would obviate the compositional problem discussed above. Then, as a final check against area-specific time effects, I control in the fifth row for a full set of region × year × year of birth effects. These estimates are generally similar to the baseline (one cannot reject the null that they are the same in any case), although the estimates incorporating area differences in time effects tend to be a bit lower. Finally, the similarity between estimates for movers and non-movers seen in Section 4 also suggests that the result is not about the local, contemporaneous wage, but instead due to influences that pre-date migration, such as early-life health.

The shift in the income/malaria relationship in Brazil is broadly consistent with a model of childhood exposure to the campaign, rather than some alternative time-series process. These results are found in Panel B of Table 4. The baseline estimates, found in the first row, are comparable to coefficients from the long-difference estimation above, and are robust to including birthplace-specific trends in the regression. (It bears mentioning the span of years in the Latin American data is much shorter than the range for the US, so horse-racing the exposure variable with second-degree trends across cohorts is a more difficult test to pass.)

The rest of Panel B examines the potential confound of contemporaneous exposure to malaria in Brazil and Mexico. Estimates on childhood exposure in the second row are produced from a specification that also includes effects of birthplace × time. On the other hand, note the data from Latin America are all drawn from censuses taken after the campaign had begun. However, the analysis for Brazil and Mexico includes data from 1960, during which time the campaigns were still in full swing. Therefore, in the third row of Panel B, I re-estimate the exposure coefficients excluding the 1960 census data. Finally, the fourth row includes a full set of region × year × year of birth effects. Point estimates that control for time effects that are differential across areas of birth are generally within a standard error of the baseline, but do tend to be lower than earlier estimates. Estimates using the ‘full controls’ are generally robust to these various checks, but, in several cases, estimates using mean-reversion and region controls only are no longer statistically significant.

Estimates for Colombia are found in Panel C. Baseline estimates, produced without controls for differential trends by area in time or cohort, are seen in columns (1) and (4) of the first row. These are similar to the magnitudes from the long-difference specification above. The second row presents specifications that include birthplace×time effects. The earliest census used for Colombia is from the 1970s, and so the check that involved dropping the 1960 census is not relevant here. Estimates for the final row produced controlling for dummies for region × census year × year of birth. Estimates are broadly similar to the baseline, even when including controls for differential trends across cohorts or across time.

Finally, Panel D reports estimates for Mexico. The baseline estimates are comparable to, albeit a bit lower than, the results for Mexico using the pre/post design above. As above, this Panel includes tests for alternative hypotheses for area-specific trends by cohort or by time. Using the basic specification with mean-reversion and region controls (Column 1)), estimates of childhood exposure remain statistically significant in the face of various checks for time effects that were differential across areas, but none of these results, including the baseline, are robust to including differential trends across cohorts (Columns 2 and 3). In contrast, when the full set of birthplace-level controls is used (Columns 4–6), estimates of the effect of childhood malaria exposure are more robust to these checks for differential trends by cohort or by time.

6.1 Normalizing by the Probability of Childhood Infection

Expanding upon the reduced-form estimates above, I renormalize the effects on adult income per probability of malaria infection. Above, data limitations required using measures of malaria that were heterogeneous across countries, but I constructed comparable reduced-form differences by comparing the most malarious to least malarious areas within each country. Representative values of these estimates are reported in the first row of Table 5, which run from 14 to 37 percent. A difficulty in interpreting these numbers, however, is that they are composed of two parts: (i) the effect on adult income of a given childhood malaria burden, and (ii) the magnitude of decline of the malaria burden following the eradication campaigns. The parameter (i) is of interest because it is portable: it is in units of income per infection rate, a number that can be applied to other situations with known infection rates. I therefore estimate the order of magnitude of (ii) and thereby can calculate the approximate effect on adult income of childhood malaria exposure in units of infection rates.

What was the range of pre-eradication malaria infection within each country? Molineaux (1988) reports on the WHO typology of malaria intensity (and associated malaria-infection rates among children): non-endemic (0%), hypoendemic (0–10%), mesoendemic (10–50%), hyperendemic (50–75%), and holoendemic (75–100%). Molineaux also reports estimates of the spatial distribution of different endemic zones throughout the world. (Both the typology and its associated geography are derived from the experience of many experts and do not simply reflect the opinion of that one author, however.) Taking the midpoint of the reported intervals, information about the types of endemicity within each country is used to estimate the cross-area differences in malaria burden prior to the campaigns. The pre-eradication malaria burden in the US ranged from malaria free to mesoendemic, representing a within-country difference in malaria-infection rates of approximately 0.3. Areas within each of the three Latin American countries varied from essentially zero to hyperendemic, for a range of 0.625 in infection probability. (These are reported in the second row of Table 5.) Because infection rates were thought to have dropped precipitously in the decade following the campaign, I take the pre-campaign level to be an adequate measure of the subsequent decline.¹³

I estimate the effect of childhood malaria infection on adult wages to be substantial: being infected with malaria through childhood lead to a reduction in adult income of approximately 50 percent. I calculate this number by normalizing the reduced-form differences with the estimated decline in malaria. (Note that this procedure has the flavor of Indirect Least Squares.) These estimates are shown in the last row of Table 5. For Brazil, the estimated effect is higher for total income (0.59) than for earned income (0.45). In Mexico, the estimate for earned income is 0.41. For Colombia, the raw estimate from Table 3 is small (approximately 0.07), but I adjust this as above using the Brazilian data as a benchmark. This reduced-form number (0.28) is re-normalized to 0.45, based on a maximal malaria infection rate of 0.625 in Colombia. In the United States, the Duncan socioeconomic index shows a larger response to childhood malaria than the occupational income score. The latter variable is calibrated using total labor income, but only incorporates across-occupation changes in income. Accordingly, it is about 25% smaller than the effect on total income for Brazil. It is unclear whether the Duncan socioeconomic index is an under- or overestimate of the full income effect, since the index effectively double counts schooling. I report it nevertheless for completeness.

6.2 Mechanisms

6.3 Comparison to Other Cohort-Based Studies of Eradication

Two other recent studies (Lucas, 2009, and Cutler et al., 2009) analyze the path of outcomes across cohorts by their effective exposure to eradication campaigns. Their methodologies are broadly similar to the ones I employ here, and so I now compare and contrast their results with those above. An advantage of these two papers over the present study is that they have access to measurements of rates of spleen inflammation across areas, which are probably better proxies of the rate of malaria infection than the endemicity variable used in Section 6.1. However, the disadvantages of these studies relative to this one are twofold. First, they assign pre-campaign malaria to individuals based on their place of residence rather than their place of birth. Thus, selective migration could be a confound.¹⁵ Second, the two other studies analyze a single cross section per episode, whereas I pool multiple cross sections to study a longer panel of cohorts. The effects of malaria, according to estimates seen above in Figure 4, play out over at least twenty years of cohorts. In a sample of less than 40 years of birth, it might be difficult to distinguish between a slow transition and a smooth trend. This might explain why the more of the emphasis in these two studies is on measuring differential effects of malaria exposure in the first few years, rather than the first few decades, of life.

Lucas (2009) shows that women born after malaria eradication in Sri Lanka and Paraguay completed more years of schooling, suggesting that returns to education rose faster than child wages in that episode. This result is consistent with positive estimates above for education in Colombia, but not with the mixed results for education in Brazil and Mexico. On the other hand, Lucas also reports estimates of the effect of childhood malaria on literacy that are similar in sign and magnitude to the estimates above for all countries (Lucas, 2009). This is consistent with a model in which childhood malaria has, to first order, an ambiguous impact on time in school, but an unambiguously positive effect on outputs such as literacy. It bears mentioning that Lucas considers ever-married females only, while the present study analyzes males only. While the underlying biological process by which malaria impedes human-capital growth might be similar across gender, the response of opportunity costs to malaria could differ between males and females.

Cutler, Fung, Kremer, Singhal, and Vogl (2009) analyze the malaria-eradication campaign in India and find malaria exposure in the first few years of life reduced household expenditures in adulthood, but had mixed effects on educational attainment. Comparing the 5th- and 95th-percentile areas, they report that the cross-cohort growth in expenditures was 3–13% higher in areas that started with higher malaria. This number is considerably smaller than the estimates above for Latin America, and probably smaller than the estimate for the US, which almost surely had less malaria in 1920 than India did in 1950. Nevertheless, there are a few methodological differences that should be taken into account. First, they compare those born after the campaign to those born before, but the earlier cohorts contains people with partial childhood exposure. Comparable years of birth for Brazil had an average childhood exposure of 0.30, and comparably lagged cohorts (the Indian campaign started about five years earlier) had an average childhood exposure of 0.43. The partial exposure of the earlier cohorts would tend to attenuate their estimates. Second, by virtue of the timing of their sample, the treatment group is quite young: the age range was 20–25 years old. It is well known that there is a ‘fanning out’ of the income distribution with age, which is in part because the return to human capital rises with age. Specifically for malaria, Hong (2007) showed that wealth accumlation was faster among twenty-somethings in areas without malaria in the 19th-century US. Moreover, if I estimate the models above (for the US) with a sample of just those 25–30 years of age, the coefficients come out about 2/3s of the average estimate. If the first and second factors compound, then an effect on log earned income of 0.27 (the estimate for Brazil) would be attenuated down to 0.08–0.12, which is within the range estimated by Cutler et al.

A.1 Details for the United States Sample

The underlying sample used for the United States consists of native-born white males in the age range [35,55] in the 1900–1990 IPUMS microdata or in the 1880 microdata from the North Atlantic Population Project (NAPP, 2004). (These data were last accessed November 14, 2005.) This results in a data set with year-of-birth cohorts from 1825 to 1965. The original micro-level variables are defined as follows:

• Occupational income score. The occupational income score is an indicator of income by disaggregated occupational categories. It was calibrated using data from the 1950 Census, and is the average by occupation of all reported labor earnings. See Ruggles and Sobek (1997) for further details.
• Duncan socio-economic index. This measure is a weighted average of earnings and education among males within each occupation. This measure serves to proxy for both the income and skill requirements in each occupation. It was similarly calibrated using data from the 1950 Census.

For the majority of the years of birth, I can compute average income proxies for all of the 50 states plus the District of Columbia. The availability of state-level malaria data and the control variables restricts the sample further to 46 states of birth. Alaska, Colorado, the District of Colombia, Hawaii, and Oklahoma are excluded because of missing data for at least one of the other independent variables. This leaves 46 states of birth in the base sample.

There are a number of cohorts born before 1885 for which as few as 37 states of birth are represented. For those born between 1855 and 1885, this appears to be due to small samples, because, while the NAPP data are a 100% sample for 1880, there are no microdata for 1890 and 1900 IPUMS data are only a 1% sample. On the other hand, for the 1843–1855 birth cohorts, all but two of the years have all 46 states represented. Nevertheless, even with the 100% sample from 1880, there are as many as six states per year missing for those cohorts born before 1843. A number of the territories (all of which would later become states) were being first settled by people of European descent during the first half of the 19th century, and it is quite possible that, in certain years, no one eligible to be enumerated was born in some territories. (Untaxed Indians were not counted in the censuses.) Note that I use the term state above to refer to states or territories. Territories were valid areas of birth in the earlier censuses, and are coded in the same way as if they had been states.

While this procedure generates an unbalanced panel, results are similar when using a balanced panel with only those states of birth with the maximum of 141 valid observations. A comparison of the cohort-specific estimates from the balanced and unbalanced panels shows high correlation (over 0.96, for example, in the case of the additional-controls specification for the occupational income score).

A.2 Details for the Brazilian Sample

The underlying sample used for Brazil consists of native males in the age range [15,55] in the 1960–2000 IPUMS microdata. (These data were last accessed April 7, 2006). This results in a data set with year-of-birth cohorts from 1905 to 1985.

State of birth is available for these samples. Brazilian states (and several territories that were to become states) were, by and large, consistently defined over the course of the sample. Those few that were not were merged together to reflect administrative divisions in the early 1950s. Specifically, I merged Rondônia into Guaporé, Roraima into Rio Branco, Tocantins into Goias, Fernando de Noronha into Pernambuco, Serra do Aimores into Minas Gerais, and Mato Grosso do Sul into Mato Grosso.

The original micro-level variables are as follows:

• Literacy. A binary variable individual measuring whether an individual can read and write at least a simple note.
• Years of Schooling. Numbers of years of education corresponding to highest grade completed. Non-numeric responses (e.g., “some secondary”) are mapped onto the midpoints of the appropriate intervals.
• Total Income. Records the total personal income from all sources in the prior month. In the empirical work above, this variable is measured in natural logs. This variable is reported in income categories in the 1960 census, and their midpoints are used in translating the data into income.
• Earned Income. Records the personal income from their labor (wages, business, or farm) in the prior month. In the empirical work above, this variable is measured in natural logs.

A.3 Details for the Colombian Sample

The underlying sample used for Colombia consists of native males in the age range [15,60] in the 1973 and 1991 IPUMS microdata. (These data were last accessed April 10, 2006). This results in a data set with year-of-birth cohorts from 1918 to 1976.

Area of birth is available in these samples at the level of departamento and municipio. The departamento is a first-order administrative division, similar to a state, while the municipio is a second-order division, similar to a county in the United States. A cohort’s municipio of birth is used in the present study to construct a proxy for childhood exposure to malaria. Colombia contains over one thousand municipios in the present day, but, to preserve confidentiality in the the IPUMS data, some of the smaller municipios are aggregated into larger groupings. This results in over 500 unique codes for area of birth, and I refer to these units simply as “municipios” in the text. Because municipal boundaries change over time, maps (SEM, 1957) and other administrative information (DANE, 2000) were used to relate data observed at various points in time onto the IPUMS recode of municipio.

The original micro-level variables are as follows:

• Literacy. A binary variable individual measuring whether an individual can read and write.
• Years of Schooling. Numbers of years of education corresponding to highest grade completed. Non-numeric responses (e.g., “some secondary”) are mapped onto the midpoints of the appropriate intervals.
• Industrial Income Score. The industrial income score is an indicator of income by industry and class of worker. It was calibrated using data from the Brazilian and Mexican censuses for all available years. To remove census-year times country effects, the starting point for this variable is log total income after being projected onto year×country effects. These residuals are then averaged by industry and class of worker and matched onto the Colombian sample. Because of the way this score is constructed, the variable is measured in natural logs. (Total income is available in the 1973 Colombian census, but the range of years of birth that these data cover is too limited.)

Control variables for the Brazilian states

• Region dummies. North (Norte and Nordeste) and South (Centro-Oeste, Sudeste, and Sul).
• Population Density. Population per square kilometer in 1950. (IBGE, 1950 and 1951.)
• Infant mortality. Number of infant deaths in the municipio of the state capital, scaled by the estimated birth rate, which is computed from data for the whole state. (IBGE, 1951.)
• Log of Electricity Capacity. Measured circa 1950. Original data in kilowatts. (IBGE, 1950.)
• Fraction of population economically active. Measured for population ten years and older for 1950. (IBGE, 1950.)
• Shares of labor force by sector. Fraction of economically active population in each of the following sectors: agriculture, extractive industries, manufacturing, transportation, and services. Measured for population ten years and older for 1950. (IBGE, 1950.)

Control variables for Colombian municipios

• Region dummies. The regions are as follows: Central, Bogota, Pacifico Norte, Eje Cafetero, Andina Norte, Andina Sur, Pacifico Sur, Caribe, Orinoquia, and Amazonia.
• “La Violencia”. A qualitative variable (ranging from 1 to 3) indicating the intensity of violence in the Colombian civil war known locally at “La Violencia”. The data are taken from Oquist, who classified conflict intensity decomposed by municipio and sub-period: before 1955, when the violence was largely in population centers, and 1955 and after, when the conflict was more likely to take place in the countryside. (Oquist, 1976.)
• High Concentration “Minifundista”. Binary variable indicating the presence of small-land holders or minifundistas, as opposed to large land holders or urban areas. The reference period is the 1950s, although land-holding patterns were persistent historically. To construct municipio-level data, the map was digitized and georeferenced. Digital data on municipio boundaries, provided under special agreement from the Centro Internacional de Agricultura Tropical (CIAT), was overlaid on the map and municipios were coded dichotomously as indicated by the map. The municipio boundaries of the CIAT data refer to 1993, and therefore these mapped back onto 1950s entities. (Banco de la República, 1964 (map 57); Jonnes and Bell, 1997; DANE, 2000; author’s calculations.)
• Coffee-growing Region. Binary variable indicating the presence of coffee cultivation. The reference period is 1960. Municipio-level data were created using the process described above for the “minifundista” variable. (Banco de la República, 1964, map 38.)
• Coal Mining Region. Dummy indicating the presence of actively exploited coal deposits, circa 1960. Municipio-level data were created using the process described above for the “minifundista” variable. (Banco de la República, 1964, map 22.)
• Expansion of Ranching. Areas identified for possible expansion of ranching in 1960. Municipio-level data were created using the process described above for the “minifundista” variable. (Banco de la República, 1964, map 55.)
• Infrastructure/Market Access. An index variable for the ease of transport to major markets or seaports from the area, based on infrastructure in circa 1960. Six (ordered) categories are used, following the map’s categorization. Municipio-level data were created using the process described above for the “minifundista” variable. (Banco de la República, 1964.)
• Level of development. An index variable for the general level of economic development of the area (“nivel de vida”), circa 1960. Six (ordered) categories are used, following the map’s categorization. Municipio-level data were created using the process described above for the “minifundista” variable. (Banco de la República, 1964, map 59.)
• Manufacturing employment per capita. Computed by municipio from the 1945 Colombian census of manufacturing. (Dirección Nacional de Estadística, 1947.)
• Disease controls. The fractions of territory within each municipio in which transmission of the following diseases occurs: leishmaniasis, yellow fever, hookworm, and non-hookworm helminth diseases. The first two categories are vector-born diseases and could themselves have been affected by the campaign. The category of non-hookworm helminths represents an aggregate of numerous types of helminths. The underlying geographic data are defined with a fairly broad brushstroke, and as a result this is almost a dichotomous variable by municipio. These data come from a GIS file provided by the Center for International Development at Harvard University, and were computed by municipio in a GIS program (the “spatial join” in ArcView). (Gallup, Mellinger, and Sachs, 1999b; and author’s calculations.)