Does more Education for the. Young increase the Wages of the Old? Evidence from School Construction in Indonesia

Transcription

1 Does more Education for the Young increase the Wages of the Old? Evidence from School Construction in Indonesia Esther Duflo August 22, Introduction Does investment in basic social infrastructure have consequences beyond the private returns for those immediately concerned? This question has potentially important policy implications, since it is often on the basis of such (presumed positive) externalities that investment in the social infrastructure is justified. Conversely, if a rapid increase in the education of young generations hurt the old generations whose human capital cannot be increased, this may make it difficult to get the old generations to finance a human capital expansion. The presence of positive externalities of education has long been hypothesized (see Schultz (167)). Human capital externalities arise when the average education of the workers in a group affects the productivity of all the other workers in the group. There is micro-economic evidence of the existence of human capital externalities in the process of development. For example, (Foster and Rosenzweig (1995) and Munshi (1999)) show that more educated people were more likely to adopt new agricultural technologies during the green revolution in India, and that PRELIMINARY AND INCOMPLETE. DO NOT QUOTE WITHOUT PERMISSION. I thank Lucia Breiova for excellent research assistance, and Abhijit Banerjee, Emmanuel Saez and Jaume Ventura, for helpful discussions. 1

2 new technologies spread through neighbors imitation. This creates a positive externality for education, since it makes unskilled farmers more likely to adopt the most productive technology. Beyond this specific evidence, it is tempting to look for human capital externalities at a more aggregate level. Several recent papers (e.g. Rauch (1993), Acemoglu and Angrist (1999), Moretti (1999)) have attempted to estimate the social returns to education, or the human capital externalities in the U.S., using wage data, at the city or at the state level. The estimation of human capital externalities using wage data can run, however, into a fundamental identification problem. The presence of human capital externalities implies that workers of a given skill level should earn more in a region with a better educated workforce, but only if the externality outweighs the mechanical decline in the marginal productivity of each effective unit of labor. The theoretical effect of an increase in the average skill level is therefore closely linked to the underlying model of the economy. In the steady state of an endogenous growth model with human capital externality (as in Lucas (1988)), all the quantities grow at the same growth rate. If there is any external effect of human capital, it will imply that the growth rate of wages will be proportional to the growth rate of human capital. In a standard neo-classical model with diminishing returns, or in the short run of an endogenous growth model (if the adjustment of the other form of capital in the economy is not instantaneous), the effect will however depend on the degree of substituability between skilled and unskilled workers. This study exploits a dramatic change in policy to evaluate the effect of a change in the effective cost of education on the average education in the labor market, and on the wages of those who did not directly benefit from the program. In 1973, the Indonesian government launched a major school construction program, the Sekolah Dasar INPRES program. Between and , more than 61,000 primary schools were constructed. In earlier work (Duflo (2000)), I showed that the program had an impact on the education and wages of the cohorts exposed to it. In this paper, I first show that the program also led to faster increases in the fraction of primary school graduates in the regions where it was more important. This increase 2

3 is strikingly similar to that which would have been predicted in the absence of any migration. I then proceed to look at the effect of the program on the wages of the cohorts that did not directly benefit from it, because they were already out of school when the program started. It turns out that wages increased less rapidly from year to year in regions that received more schools. This holds even after controlling for the factors that determined the initial allocation, and may have caused different growth trajectories across these regions. Using interactions between the survey year and the number of INPRES school per 1,000 children as instruments for the fraction of educated workers in the region therefore suggests a negative effect of the proportion of primary school graduates on individual wages, keeping the individuals own skill level constant. This suggests that the externality of human capital at the regional level, if any, is smaller than the mechanical effect of an increase in effective labor supply. The remainder of this paper is organized as follows: In section 2, I describe the INPRES program and its effects on average education. In section 3, I discuss the identification of the effects of the average education on individual wages and derive the empirical specifications. Section 4 presents and discusses the results. Section 5 concludes. 2 The program and its effect on average education 2.1 The Sekolah Dasar INPRES program In 1974, the Indonesian government initiated a large primary school construction program, the Sekolah Dasar INPRES program. Between 1974 and 1978, 61,807 new buildings were constructed, which doubled the number of available schools per capita. More schools were put in regions where initial enrollment rates were low, which caused important regional variations in the intensity of the program. Using a large household survey conducted in 1995 (the SUPAS 1995), I linked to the number of schools constructed in each individual s region of birth, Duflo (2000) showed that the growth in education between cohorts unexposed to the program and cohorts exposed to the program was faster in regions that received more INPRES schools. This 3

4 difference can be attributed to the program with a reasonable level of confidence, because this pattern is not present among cohorts who were not exposed to the program. In addition the program affected mostly primary school completion, whereas omitted factors would have affected other levels of schooling as well. This pattern is summarized in figure 1, reproduced from Duflo (2000). Each point on the solid line summarize the effect one more school built per 1,000 children had on the average education of children born in each cohort 1. Children in Indonesia go to primary school until age 12 (although delay at school entry and repetition are not uncommon), therefore one would expect the effect of the program to be 0 for children who reached 12 before 1974, when the first schools were built, and to be progressively increasing. This is exactly what the picture shows. If migration flows were either small or not affected by the program, one would expect to see a similar pattern when comparing the evolution of average education over the years in the different regions. As the generations exposed to the program enter the labor market, one should see the average education (and in particular the fraction of primary school graduates) increase faster in the regions that received more schools. 2.2 Data and empirical specification The data for this paper come from the annual Indonesian Labor Force Survey (SAKERNAS), from 1986 to These surveys are repeated cross sections, of approximately 60,000 households. The surveys contain information on province and district of residence (but not of birth), education level achieved, labor force participation, type of employment, number of hours worked per week and wages for individuals who work for a wages. I restrict the sample to males aged 20 to 60, and I exclude Jakarta. 2 Descriptive statistics are presented in table 1. The fraction of individuals born after 1962, and therefore theoretically exposed to the program, in the 1 These are the coefficients obtained by regressing years of education on the the interactions between the number of schools built per capita in the individual s region of birth and year of birth dummies, after controlling for year and region of birth fixed effects. 2 Results do not depend on this exclusion. 4

5 age groups and 20-60, increases progressively over the years. I consider the proportion of primary school graduates in each region in each year. There is a total of 3826 district-year cells, with an average of 287 individual observations in each cells in the full sample. 3 All the regressions are performed on this aggregate data set, and each cell is weighted by the number of observations used to construct it. Consider comparing two regions in 1986 and 1999, one of which received a large number of INPRES schools per capita, and the other one a small number of schools. The fraction of people who were young enough to be exposed to the INPRES program is bigger in 1999 than in We know that the gains in years of education of these younger cohorts, relative to the older ones, were bigger in the regions that received more schools. If the effect of the program was not undone by migration, one would expect the average education (in particular, the proportion of primary school graduates) to have grown faster in the region that received the most schools. This suggests comparing the difference in educational attainments between 1999 and 1986 in these two regions. More generally, this suggests that, if one runs a regression of the difference between average educational attainment in 1999 and 1986 on the number of schools per capita built in each region, one should see a positive coefficient. Finally, this reasoning applies to any year-to-year difference. In summary, this suggests the following specification: S jt = α t + γ j l=1987 (λ l P j )γ 1l l=1987 (λ l C j )δ 1l + ɛ jt (1) where S jt is the proportion of primary school graduates among adults in year t in region j, α t is a survey year fixed effect and γ j is a region fixed effect, P j is the number of INPRES schools built between 1974 and 1978 in region j, and λ l is a survey year dummy (λ l = 1 if t = l). C j is a vector of initial conditions that are introduced as control variables. In particular, it may be important to control for the enrollment rate in 1971, since it was a determinant of the placement of the program. Note that the first order effect of a higher enrollment rate in 1971 is a difference in level 3 There are on average 185 observations per cell of individuals born before 1962, including 61 with wage data. 5

6 of education, which should affect all cohorts, and all survey years identically, and therefore be absorbed by the region fixed effect. Only a change in the rates at which children attend school in a region will lead to a change in the rate at which average education increases from year to year. Therefore, controlling for the enrollment rate in 1971, interacted with year dummies, is important only to the extent that we think changes in enrollment rates are correlated with levels. I also control for the number of children in Results Since the generations exposed to the program have already started entering the sample in 1986, one would expect all the coefficients to be positive and increasing. Columns 1, 2, 4 and 5 in table 2 show these coefficients for the specification which includes enrollment rates as a control, for adults aged 20 to 40 and for adults aged 20 to 60, in the whole sample and in a sample which excludes urban regions. 4 The fraction of young (or exposed) people among individuals aged 20 to 40 increases faster than among those aged 20 to 60, and one would expect the coefficients to be larger and more significant in the former group. The group of individuals aged 20 to 60, however, corresponds better to the labor market, and will therefore be important in the second stage of this analysis. The coefficients are increasing for both groups, they are jointly significant, and, as expected, they are larger in the group aged 20 to 40. They become individually significant from 1991 in the group and from 1996 in the group. Since all the coefficients are expected to be positive, it is not possible to use pre-program data to test the identification assumption that the increase in education levels over time would not have been systematically different in regions where a different number of schools were built, even in the absence of the program. If migration equalized education levels across regions, this would have led to a similar pattern. If this were the case, one would see a faster increase in the education over the years, even in the subsample of those who were not exposed to the program (individuals born in 1962 or before). To check this, I estimated a specification similar to equation 4 The specification without enrollment rates as a control is very similar, and is therefore omitted. 6

7 1, with the fraction of primary school graduates among individuals born in 1962 or before as the dependent variable. The coefficients are presented in columns 3 and 6 in table 2. Figure 2 gives a graphical summary of these estimates: It shows the coefficients (and their confidence intervals) for the entire group aged 20 to 40, and for the group of individuals born before There is no systematic increase among older people. The coefficients in the two equations are significantly different from each other. This results is interesting in two respects. First, it reinforces our confidence in the interpretation that the faster rate of increase in the number of primary school graduates in regions that received more schools can indeed be attributed to the program. Second, it suggests a strategy to look at the effect of an average increase in education, keeping constant the individual level of education: the interaction of the survey year and the number of INPRES schools constructed in each regions predicts average education, but it does not predict the education among older people. It therefore suggests that by restricting the study to this group, one can obtain estimates of the effect of average education on individual wages, net of any effect of own education. Our focus in the next sections of this paper will therefore be the effect of the program on the wages of the old (unexposed). 2.4 Does migration undo the effect of local infrastructure development? The results in the previous section already suggest a partial answer to this question. Since the program affected the average education of adults, it indicates that its effects were not totally undone by migration. We can, however, make this result more precise by comparing the effect the program should have had, in the absence of any off-setting effect of migration, with the effect it had in reality. The results from this exercise are important in the context of an increasing focus on decentralization, notably in Indonesia. If local governments consider that the communities are not getting any benefits from investment in education because educated people migrate (with their human capital), decentralization of school finance may lead the public financing of education to decline. To get at this question, I first estimated the effect of the number of INPRES schools con- 7

8 structed per capita in an individual s region of birth on the probability that an individual completed primary school, for each cohort. To this end, I used the SUPAS 1995 data, which contains the individual s region of birth. I regressed a dummy indicating whether an individual completed primary school on a set of region of birth fixed effects, cohort of birth fixed effects, and interactions between the number of schools constructed in one s region of birth and year of birth dummies. The equation estimated is identical to equation (11) in Duflo (2000), except that it used the primary school completion as the dependent variable. Denote the effect of the program on the cohort born in year k as π k. I used the 1995 data to compute the proportion of primary school graduates among those aged 20 to 40 in each year (from 1986 to 1999) born in each region before Denote this average S oj. For each survey year, note φ kt the share of those aged 20 to 40 who were born before 1962, in 1962, in 1963, etc. Finally, I computed the proportion of primary school graduates that would have been predicted for each region and each year in the absence of migration (and if the program effect had been the same in all regions) as: ( t 20 S jt = S oj + P j k=1962 π k φ kt ) Note that this predicted value does not contain any information specific both to the region and the year considered. There is therefore no source of mechanical relationship between S jt and S jt. The first observation is that S jt and S jt are strongly correlated. The regression of the actual share of primary school graduates on the predicted share leads to a coefficient of 0.84, with a t. statistic of 77). This is not very informative, because a large part of this correlation is driven by the old, and would therefore still be there even if all the educated young had migrated out of the high program regions. The following experiment is more informative. I run the same specification as in equation 1, but I use as dependent variable the predicted education, S jt. These coefficients indicate how the average education of adults would have been affected in each region in the absence of any offsetting effect of migration. The coefficients γ 1l obtained in this specification are plotted in figure 3, along with the coefficients obtained when estimating equation 1 with the actual average as the dependent variable. The two sets of coefficients are (2) 8

9 surprisingly close to each other. In particular, there is no evidence that the predicted effect is bigger than the actual effect. These results need to be placed in the context of relatively low migration flows. In 1995, if one excludes Jakarta, 12% of individuals in the SUPAS sample did not live in their province of birth, and 24% did not live in their district of birth (17% if one excludes the urban regions). 3 The effect of average education on individual earnings: model and identification 3.1 Conceptual framework In a developing economy, fixed factors (such as land) play a potentially important role, at least in the short run. For this reason, using a neo-classical production function with diminishing returns to human and physical capital combined (in the absence of externality) seems reasonable. We assume that each district forms a distinct economy, and that the aggregate production function in each district is Cobb-Douglas, with the form: Y = (AT ) β H α K 1 α β H γ K δ, (3) where T represents land, H represents human capital and K represents physical capital. Constant returns apply at the level of the individual firm, but the average level of H and K appear as additional inputs (with an exponent γ and δ, respectively). For simplicity, we assume that the population is normalized to 1. Consider the simple case where, in the absence of any government intervention, the stocks of human and physical capital evolve according to: Ḣ = s H Y δh, and K = s H Y δk. 9

10 s h and s k are reduced form parameters, which we could derive from time preference of the individuals. This economy can exhibit endogenous growth if γ + δ β. Suppose that educated and uneducated workers are perfect substitutes: H = S 0 + S 1 h 1 + S 2 h , where S 0 is the number of uneducated workers (who did not graduate from primary school), S 1 is the fraction of workers who graduated from primary school, etc...this is clearly a strong (and certainly wrong) assumption, but we can see whether the data support its predictions. The wage of an unskilled worker at date t is given by: ln(w 0t ) = β ln(a t ) + ln(α) + β ln(t ) + (α 1 + γ) ln H t + (1 α β + δ) ln K t (4) The wage of a skilled worker is just the wage of an unskilled worker multiplied by a constant. Consider running an OLS regression of the wage of an unskilled workers on ln(h t ). Because K t, T and A t are omitted, the OLS coefficient would be a biased estimate of (α 1 + γ). In particular, theory predicts that K t and H t are positively correlated. If the model has a steady state, the steady state levels of K/A and H/A are both functions of s h, s k, the growth rate of A and δ, which means that they are closely linked. If the model exhibits endogenous growth, the ratio K/H is constant, they are therefore perfectly correlated. It is also likely that H t would be correlated with A t and T since they enter as factors in its production. It is therefore unlikely that one can learn very much from this regression unless one has excellent capital data, land data, and data about all the factors that enter A. The early attempts to identify human capital externalities relied on the comparison of a cross section of cities. Rauch (1993) showed that wages in cities are positively correlated with the average education of the workers in the city, after controlling for each individual s education. To justify his specification, he used a model of location choice where the cost of living compensates the increase in real wages, and the average level of education in each city is the result of historical accidents. Moretti (1999) argued that treating average education as randomly assigned can be misleading if the average productivity in regions where workers are more educated is higher for 10

11 some other reason, and proposed looking at differences in wages in a given city over time. Consider the growth rate of w 0 : w 0 A = β w 0 A + ln(α) + (α 1 + γ)ḣ H + (1 α β + δ) K K (5) Again, an OLS regression of the growth rates of wages on the growth rate of human capital, without controlling for the growth rate of physical capital, will not produce consistent estimates of (α 1 + γ). instrument for Ḣ H Ḣ H and K K will almost certainly be correlated.5 Moretti (1999) proposed to with the share of young people in the base year. Because young people get more education than old people, the average education will grow faster in regions which have more young people. The difficulty with this particular strategy is that the share of young people in the base year is very likely to influence physical capital accumulation. 6 In the Indonesian case, a potential instrument for Ḣ H is the number of primary schools constructed by the INPRES program. To understand how the instrument works and its limitations, suppose first that the government allocated the schools randomly. Each school reduces the effective cost of schooling, and therefore increases the enrollment rate among all the future young generations (but not that of the old generation). Note that, contrary to what is often assumed 5 If one assumed that the economy was on an endogenous growth path, H and K would grow at the same rate, therefore one would obtain an estimate of γ + δ β, which would have to be positive for the assumption to be satisfied 6 Acemoglu and Angrist (1999) proposed to use changes in compulsory schooling laws as instruments for In this model, changes in compulsory schooling laws are a good instrument for Ḣ H Ḣ H. if it is not related to K K.The question does not arise in the model they emphasize, which comes from previous work by Acemoglu (Acemoglu (1996)). The labor market is not competitive: all the firms are matched with a worker, they produce and as a result of bargaining each worker gets a fraction of the output. Investment is realized by firms before they are matched with a worker, and they do not know which workers they will be eventually matched with. The stock of physical capital adjusts immediately to an increase in the stock of human capital, because firms invest more in anticipation of the average human capital of the worker they will employ in the future. In this world, the externality comes precisely from the relationship between provides a realistic description of the Indonesian economy of the period. Ḣ H K and. It is however unlikely that this model K 11

12 in the macro-economic literature (e.g. Mankiw, Romer and Weil (1992)) enrollment rate is not the analogue of savings rate. Because generations succeed each other and the new generations are born with no education, a constant enrollment rate would maintain a constant level of human capital, not increase it. The net rate of increase of human capital is the enrollment rate of the new generation entering the labor market minus the enrollment rate of the old generation leaving it. The increase in the number of schools combined with the fact that the young generations progressively enter the labor market changes Ḣ Ḣ H. The modification in H is a function of the number of schools built, which suggest that if the schools had been allocated randomly, the number of INPRES schools would form an ideal instrument. In practice, however, the government allocated more schools in regions where enrollment rates at the primary school level were lower. The evidence presented in this paper and in Duflo (2000) suggest that the rate of growth of human capital was not systematically correlated with the program before it was initiated. Still, the level of the program will not be a valid instrument for Ḣ H in this context if it is correlated with Ȧ A or neo-classical case, a correlation between the program and K K K K. We cannot say much about Ȧ A. In the will arise if regions which received more schools were systematically closer to or further away from their respective steady state. A natural presumption would be that regions that received more schools, which were poorer, would be further away from their steady state. This would lead to a positive correlation between the program and K K, and therefore lead the coefficient of Ḣ H to be biased upwards. To control for this, we will control for the amount of convergence predicted by the 1971 enrollment rate. In addition, we will present a specification controlling for a convergence term (the level of wage in the base year). In practice, Indonesian provinces exhibited very little convergence in gross provincial product per capita until 1996 (Hill (1996)). The Indonesian crisis, however has hit richer regions, and in particular cities, much more than poorer and more rural areas (Frankenberg, Thomas and Beegle (1999)). This will tend to generate a convergence in average wages, since rural areas received more schools. It should appear as a break in the trend in the reduced form, and should not be a serious problem if we restrict the sample to rural areas of to 12

13 the pre-1997 period. One can also imagine that the modification in the growth rate of human capital endogenously induced an increase in the investment in physical capital. For example the imbalance in the relative levels of human and physical capital would lead to a faster rate of growth in physical capital than human capital in an endogenous growth model. (see Barro and Sala-I-Martin (1995)). In this case, the instrumental variable strategy will pick up not only the pure sum of the labor supply and technological externality, but the indirect effect through physical capital accumulation as well Empirical specifications The INPRES program affected essentially the proportion of primary school graduates. To simplify the notation, we will assume for that two skill levels have been achieved in the economy: no education, and primary school or above. 8 This implies that H jt = (1 S jt ) + S jt h, where S jt is the proportion of primary school graduates and h is the ratio of their productivity to that of the uneducated. The assumption of perfect substitution implies that for any given worker, ln(w ijt ) = S i h + ln(w 0jt ) + υ ijt, (6) where S i is a dummy indicating whether the individual has graduated from primary school. The error term υ ijt reflects all the other factors that determine wage, besides own and average education. The effect of the average education on the logarithm of wages should therefore be the same for all skill groups (this is a testable implication of the assumption of perfect substitution). Substituting the expression for ln(w 0jt ) from equation 4 and including all the variables which we do not measure in the error term, we obtain a relationship between individual wage, individual education level, and regional human capital in the region at date t. 7 For Acemoglu (1996), the externality comes precisely from the fact that a greater share of educated workers leads to bigger investments in human capital. 8 It is important that the other skill levels are achievable, even though they have not been attained yet, to leave open the possibility of permanent accumulation of human capital. 13

14 ln(w ijt ) = S i (h 1) + (α 1 + γ)(h 1)S jt + ɛ jt + µ t + ν j + υ ijt, (7) where µ t + ν j + υ ijt = β ln(a jt ) + ln(α) + (1 α β + δ) ln K jt + β ln(t j ), and we used the approximation: ln(h jt ) = ln((1 S jt ) + S jt h) (h 1)S jt As we have seen, estimating this equation by OLS could be very misleading, because of the correlation between ɛ jt and ln(h jt ). Acemoglu and Angrist (1999) show that there is an additional problem. If for any reason, the coefficient of individual schooling is not properly measured, there will be a spurious coefficient of average schooling in a wage regression, even if there is no correlation between ɛ jt and S jt, and even in the absence of any effect of average schooling on wages. Specifically, Acemoglu and Angrist (1999) show that the coefficient of the fraction of primary school graduates in this regression is equal to φ(ρ 0 ρ 1 ), where ρ 0 is the coefficient from a bivariate regression of ln w ijt on S i, ρ 1 the coefficient from a bivariate regression of ln w ijt on S jt (this is the 2SLS estimate of the effect of individual education on wages using region dummies as instruments), φ = 1 1 R 2, and R 2 is the R-squared from a regression of S i on the region dummies. So if for any reason, the OLS and the 2SLS estimates of returns to education are different, π 1 will not be equal to zero. Acemoglu and Angrist (1999) propose to instrument both for S i and S jt. A conceptually simpler alternative is to find a valid instrument for S jt which does not affect S i. In this case, it is easily seen that the 2SLS coefficient of S jt using this instrument will consistently estimate the effect of average schooling on individual earnings. Further, controlling for individual education will not affect the coefficient of average schooling. Clearly, it is not possible to find such an instrument for all individuals in each region j; however, there may be some individuals for whom it is going to be the case. The nature of the INPRES program suggests both the instruments variable strategy and the group whose education was not affected: all individuals who were born in 1962 or before were not affected by the program and we have verified in the previous section that the average education in this group did not grow faster from year to year in the regions that received more 14

15 INPRES schools). Take the average of equation 7 for all individuals born before 1962: ln(w ijt ) = S jto (1 h) + (α 1 + γ)(h 1)S jt + µ t + µ j + υ ijt, (8) where S jto is the proportion of primary school graduates among the old in year t in region j. Under the conditions discussed in the previous sub-section, we can take the first difference of equation 8 and use the number of INPRES schools (P j ) as an instrument for S jt S jt 1, possibly after controlling for some control variables such as the enrollment rate and the wage in 1986 (a vector C j ). Interacting these control variables with survey year dummies will allow us to control for some aspects of the different dynamics of these regions over time. Thus the reduced form with two years of data would be written: ln(w jt ) ln(w jt 1 ) = C t + ζ 0 P j + ζ 1 C j + ξ jt Note that (S jto S jto )h is not correlated with with P j, and is now part of the error term. This equation can be generalized to incorporate all available years, leading to a reduced form equation similar to equation 1: ln w jt = α t + γ j l=1987 (λ l P j )γ 2l l=1987 where α t and γ j are year and region fixed effects, respectively. (λ l C j )δ 2l + ɛ jt, (9) Equations 1 and 9 form respectively the first stage and the reduced form of an instrumental variables strategy to estimate equation 8. We can also estimate equations similar to equation 8, using alternative dependent variables: the average residual wage (obtained from regressing ln wjt on own education and age dummies), the wage of the uneducated only, the wage of the educated only, and the skill premium. We should find that all the coefficients on average wages in the various groups are similar and that the skill premium is not affected, under the joint hypotheses that the assumption of perfect 15

16 substitution is valid, that own education is exogenous, and that the program did not affect the education of the old. 4 Results 4.1 Reduced form results The reduced form results (the estimates of the coefficients γ 2l in equation 9) are presented in table 3 and in figures 4A and 4B. These two figures summarize the reduced form results. Although none of these coefficients is individually significantly different from zero, they are declining, in contrast to the coefficients of average education, which were increasing. In the sample that includes both urban and rural areas, the coefficients increase from 1997 to 1999, which most probably reflects the differential impact of the crisis. In the rural sample, they are monotonically declining. 4.2 The effects of average education on individual wage The main sample for the analysis is all the individuals aged 20 to 60 who are born before I will consider two independent variables. First, the fraction of primary school graduates in the sample aged 20 to 60 (a reasonable approximation of the average education in the labor market); second, the fraction of primary school graduates among the The INPRES program directly affected the later (since the older affected people were 37 in 1999). The former was affected as a consequence: Focusing on the variable puts more accent on the source of identification. 10 Table 4 presents OLS estimates for equation 8, where the dependent variable is the average 9 It means that when we change year, there is both a cohort effect and an age effect. I have run all the specifications in a cohort which maintains a constant cohort, and the results were very similar. 10 In addition, the first stage is stronger for this variable, which minimizes the problems that can arise from using weakly correlated instruments. One would expect the results with the average to be a scaled up version of the results obtained with the average. 16

17 wage and the average of the residual wage (after controlling for individual education and age). The first panel does not include region fixed effects, while the second one does. As expected, results obtained from specifications that do not control for individual education are bigger. They lump together the social and the private returns. We should, therefore, focus on the coefficients of average education in the wage residual equation. The difference between the first and the second panel illustrate the remark we made in the previous section: the OLS estimates are much bigger than the corresponding fixed effects estimates, which suggests that they are very strongly upward biased (Acemoglu and Angrist (1999) obtain the same results): educational attainments are higher in regions where wages are higher, but it is as likely to come from a relationship running from income to education as from the opposite relationship. 11 The OLS results are all positive and significant, while the OLS results with fixed effect are positive, but significant only in the specification that has the proportion of primary school graduates among those aged 20 to 60 as the dependent variable. These point estimates suggest small positive effects: an increase of 10 percentage point in the share of primary school graduates among those aged 20 to 60 is associated with an increase of 0.8% in the wages, after controlling for individual education. These coefficient are more than ten times smaller those estimated by Moretti (1999) for the impact of the share of college graduates in the US. They are more in line with the small coefficients of Acemoglu and Angrist (1999), who use the the average educational attainment as the dependent variable, but identify it essentially out of variation in the share of graduates from secondary school. Table 5 present the instrumental variables results. The results are presented for the entire sample, and in a sample that excludes the years 1998 and 1999, since the crisis hit different regions differently. The immediate observation is that all the coefficients in this table are nega- 11 There are many reasons, besides those emphasized here, which would lead OLS coefficient to be biased upwards. First, there may be wealth effect in education: Glewwe and Jacoby (2000) find important wealth effect in Vietnam. Second, with economic growth, expected returns to education improve, and this may lead to a higher demand for education (see Foster and Rosenzweig (1996) for micro-economic evidence of the Indian green revolution, and Bils and Klenow (1998) for a re-interpretation of the cross-country in these terms. 17

18 tive. In the full sample, the estimates become more negative when the crisis years are taken out. It does not affect the estimates in the rural areas. The estimates obtained using the residual wage or the actual wages as the dependent variable are very similar, which is reassuring. The estimates using the residual wage are somewhat more precise. They suggest that an increase of 10 percentage points in the share of primary school graduates among the 20 to 60 year old led to a decrease of 3.8% in wages in full sample, and to a decrease of 9.9 % in the sample of rural areas. Without using the last two year of data, the coefficients are respectively -4.3% and -9%. The negative coefficient is significant in the rural sample. If we focus on the share of primary school graduates among the 20 to 40 year old (for which the first stage has more power), the story is the same: an increase of 10 percentage point in the share of primary school graduates leads to a decrease of 2.9 % in the wage of the old in full sample, and to a decrease of 6.3% in the rural sample, and the number is significant in the rural sample. When we control for the wage in 1986 interacted with the year dummies (to account for the rates at which wages in these regions would have grown in the absence of the program), the coefficients become more negative in the combined sample, and stay essentially the same in the rural sample. Table 6 presents the results broken down by education level, as well as the effect of share of primary school graduates on the primary education premium. I do not report the OLS results without region dummies, which have been shown to be very strongly upwards biased. The OLS estimates (with region dummies) show a small and insignificant negative impact on the skill premium. The IV point estimates are either negative or positive, totally insignificant, and within the confidence bands of the OLS results: there is no strong evidence against the hypothesis of perfect substitution in this table. These results suggest that the effect of an increase in the average education of the young generations is to decrease the wage of the old generation, who did not directly benefit from the program. Are the estimated parameters compatible with the simple model we have outlined? If the model were strictly exact, we would be estimating the parameter(α 1 γ)(1 h). The 18

19 average h estimated in is around The point estimate is in the full sample. For this to be compatible with this model, that would imply that alpha + gamma is 0.2, which does not seems reasonable. 12 Some underestimation of the skill premium would go part of the way, but this suggests that one effect of the program was overlooked or that our production function was miss-specified. Below, we explore the role played by participation in the formal labor market. 4.3 Formal labor force participation The last column in table 6 presents the results using an alternative dependent variable, the fraction of the sample who work for a wage (instead of being self-employed). The average fraction of individuals working for a wage fluctuates between 30% and 36% from year to year. Both the OLS and the 2SLS estimates suggest that there is a strong positive effect of the fraction of primary school graduates on the probability that someone works for a wage. A 10% increase in the proportion of primary school graduates leads to a 4.5% increase in the probability of working for a wage. These estimates are robust to all the alternative specifications that we discussed for the wage regressions. This result invites four directions of exploration. First, is it genuine? Second, how does it affect the previous results on wages? Third, can it help understand the magnitude of the coefficient? Fourth, how can we interpret it in light of the reduction in wages? After controlling for the number of children in 1971 in the region, the probability of working for a wage is not correlated with the intensity of the program. The pattern, therefore, does not seem to be caused by mean reversion in the number of individuals working for a wage. To check for this, I controlled for the initial level of participation interacted with year dummies. The pattern persists. In addition, the coefficient is unaffected when we estimate the coefficient within sub-groups of regions with similar levels of initial participation. The results are unchanged as well when I use as dependent variable the residual of a regression of participation on education and wages. This result seems therefore to be very robust. It echoes the findings in Duflo (2000) 12 Doing the same calculations in the rural sample deepens the puzzle, since the corresponding estimate is -0.9, which would require α + γ to be negative! 19

20 and Spohr (2000) that own education increases the probability that someone participate in formal employment. Does it affect the validity of the 2SLS results on wages? In principle, it could, since the probability of selection in the sample is affected by the instruments. In particular, one can imagine a situation where the program pushed the marginal self-employed into the formal labor force, and these marginal employees receive a lower wage. Moreover, new entrants into the labor force have a lower experience, which should lower their wages. To assess this hypothesis, I examined whether the program affected the ratio of the income of wage earners to that of non-wage earners. I used the incomes modules from the SUSENAS from 1987 and 1993 and computed the ratio of the income of self employed to the income of wage earners. The ratio is very stable between 1987 and 1993: self-employed earn 17.85% less than employed in 1987, and 18.5% less in I then regressed the difference in the log of this ratio on the level of the program, and found no relationship (the coefficient of the INPRES program is , with a absolute t statistic of 0.130). It seems that the relative wage loss of the old generation in regions where the program increased the supply of primary school graduates cannot be attributed to a decline in the ratio of the earnings of wage earners to those of non wage earners. It remains that the increase in labor force participation would have caused the effective labor supply to go even further up. To empirically asses the importance of this effect, I used a statistical sample correction strategy along the lines proposed by Heckman and Hotz (1989). The idea is to control for the propensity score, or the probability of being selected in the sample given the instruments. The model is still identified because there is more than one instrument. The analogue in this case is to regress the share of the sample who works for a wage on the instruments, and to control for the predicted value from that regression in the second stage of the wage regression. These estimates are therefore the effect on the wage, keeping constant the labor supply. The results of this sample selection correction are shown in column 5 of table 6. The point estimates are smaller in absolute value: in the full sample they go down from to -0.15, in the rural sample they go down from to If we take these point estimates 20

21 seriously, they would imply an estimate of α + γ of 0.73 in the full sample, and 0.32 in the rural sample. These are more reasonable (although still small in the rural case), but are certainly not compatible with large positive externalities. These estimates are, however, imprecise. Alternatively, we can start from our baseline estimate, and take into account the increase in labor supply induced by an increase in the number of primary school graduates. We estimated that an increase of 1% in the number of primary school graduates led to an increase of 0.44% in the participation rate. The number is similar for educated and non educated. This means that the increase in effective labor supply caused by an increase in the share of primary school graduates is not h 1, but h (1 + S(h 1)) 1, which is equal to 1.16 at the average sample value of S of 0.7. Our baseline estimates now imply (α 1 + γ) = 0.37 in the full sample (i.e. α + γ = 0.63), and (α 1 + γ) = 0.78 in the rural case i.e. α + γ = 0.22). 13 Interestingly, these calculation bring us fairly close to the numbers implied by the corrected estimates. However, we are now left to explain how average education could have the seemingly contradictory effects of reducing wages (for a given participation rate) and increasing wage employment. This result violates the assumption that educated and uneducated are perfect substitutes, and suggest, once again, that the simple model we outlined is not an accurate description of the economy. A model that would reconcile both findings is on in which people with some education can be employed either as manual labor or as manager. A manual laborer can be either rent land from a landowner, or be combined with land, capital and a manager in a firm. As the supply of potential manager and the efficiency of manual labor increase, landowners take out some of their land to the labor market, and hire instead laborers for estate farming. Preliminary evidence suggests that the program did not cause a reduction in the increase of graduates from junior high school (despite causing some increase in their numbers). It may suggests that they benefit from being combined with more efficient labor. Future work should use richer sources of 13 Clearly, these calculations are wrong, since the approximation ln(1 + S) = S is not valid when S becomes close to 1. 21

22 data to evaluate whether the empirical implications of this story are verified. 5 Conclusion This paper argued that the SD INPRES program, a large school construction program undertaken by the Indonesian government in the 1970s, constitutes good case study to empirically examine the impact of average primary schooling on the wages of older cohorts. This experiment modified the enrollment rates for the young generations, thus inducing a very long lasting change in the rate of human capital accumulation in the regions it affected most. The impact of this shock on the supply of educated workers can be studied on an old generation, who did not directly benefit from it. It provides a very natural solution to the identification problems inherent to any attempt to identify the effect of the average of a regressor while trying at the time to control it. These exercises are typically motivated by the attempt to identify social capital externalities. However, if there is any factor that stays fixed (at least in the short run), this type of exercises can identify only the sum of the traditional labor demand effect and the human capital externality. Most of the empirical work in macroeconomics is based on the idea that countries are converging toward a steady state (Barro and Sala-I-Martin (1995)), and this seems to be a reasonable starting point when studying a developing economy. Correspondingly, the instrumental variables estimates presented in this paper suggest that the effect of average education on individual wages (keeping the skill level constant) is negative. This is in sharp contrast to the OLS estimates, who are strongly positive, and to the fixed effect estimates, who are closer to zero, but still positive. Such a strong bias in the OLS estimates suggest that the cross-country relationship between output per capita is likely to be affected by the same upward bias. This evidence suggests that the cross-sectional relationship between education and income levels should not be used as the basis of an argument for the public funding of education. It does not imply, however, that education should not be funded publicly. First, this paper 22

23 essentially shows that externalities cannot be identified from wage data, even micro-data. The mechanism through which potential externalities arise must be explicitly discussed and tested (the literature on learning and technology adoption is a good example of this line of research). Second, externalities are but a piece of the story which explain why education level achieved without government intervention can be sub-optimalbanerjee (2000). All it suggests is to exert caution when using the available evidence. References Acemoglu, Daron (1996) A microfondation for social increasing returns in human capital accumulation. Quarterly Journal of Economics 111(3), Acemoglu, Daron, and Joshua Angrist (1999) How large are the social returns to education? Evidence from compulsory schooling laws. Mimeo Banerjee, Abhijit (2000) A dynamic framework for educational policy. Mimeo, MIT Barro, Robert, and Xavier Sala-I-Martin (1995) Economic Growth (Mc Graw Hill) Bils, Mark, and Peter Klenow (1998) Does schooling cause growth or the other way around? WP 6393, National Bureau of Economic Research Duflo, Esther (2000) Schooling and labor market consequences of school construction in Indonesia: Evidence from an unusual policy experiment. MIT Working Paper Series, Foster, Andrew D., and Mark R. Rosenzweig (1995) Learning by doing and learning from others: Human capital and technical change in agriculture. Journal of Political Economy 103(6), (1996) Technical change and human-capital returns and investments: Evidence from the green revolution. American Economic Review 86(4),