The World Bank Economic Review, 38(2), 2024, 351–370 https://doi.org10.1093/wber/lhad036 Article The Short- and Longer-Term Effects of a Child Labor Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 Ban Caio Piza, André Portela Souza, Patrick M. Emerson, and Vivian Amorim Abstract This paper investigates whether the 1998 Brazilian law that increased the minimum employment age from 14 to 16 lowered child labor and increased school attendance and whether those effects persisted beyond age 16. Using a regression discontinuity design, the results indicate that the ban had a significant impact on urban boys, a cohort that represents half of all paid child labor in Brazil. This cohort had a 35 percent decrease in paid labor, driven mainly by a decrease in informal work, and an 11 percent increase in the share of those only attending school. In addition, there is evidence that these effects persist past the age of enforcement where the affected cohort was less likely to work and more likely to be only attending school beyond age 16. Overall, the results suggest that enforced bans on child labor can have significant immediate and persistent impacts on affected populations. JEL classification: C21, J08, J22, J24, K31 Keywords: child labor, regression discontinuity, local randomization, minimum employment age 1. Introduction Numerous studies have shown the deleterious effects of working as a child, particularly at younger ages. Though child-labor rates have been declining worldwide, the numbers are still alarmingly high. In 2020, the International Labor Organization (ILO) estimated that 160 million children aged 5 to 17 were work- Caio Piza is a senior economist at the Development Impact Evaluation Unit at the World Bank, Washington DC, United States; his email address is caiopiza@worldbank.org. André Portela Souza is a professor at the São Paulo School of Economics, Getulio Vargas Foundation (FGV), São Paulo, Brazil; his email address is andre.portela.souza@fgv.br. Patrick M. Emerson is a professor at the Oregon State University, Corvallis, United States; his email address is patrick.emerson@oregonstate.edu. Vi- vian Amorim is a consultant of the World Bank, Washington DC, United States; her email address is vamorim@worldbank.org. The authors thank Prashant Bharadwaj and the participants of the seminars at the World Bank (DIME Seminar Series), Sao Paulo School of Economics, EPGE-FGV RJ, Brazilian Econometrics Society, the World Bank ABCDE Conference 2015, and the EEA-ESEM 2017 for their comments. The authors thank DIME i2i, the Brazil Country Office, and the World Bank Devel- opment Economics Vice Presidency (DEC) for their financial support. André Portela Souza thanks the World Bank for financial support for research while he was a visiting researcher in DEC. The data that support the findings of this study are openly available in the Brazilian Institute of Geography and Statistics at https://loja.ibge.gov.br/pnad- 1987- a- 1999- microdados.html (1998 and 1999 waves of the Brazilian Household Survey) and https://www.ibge.gov.br/estatisticas/sociais/educacao/9127-p esquisa- nacional- por- amostra- de- domicilios.html?t=microdados (2001 to 2015 waves of the Brazilian Household Survey). Our code is publicly available at https://github.com/worldbank/child- labor- ban- brazil. It allows the replication of all the tables and figures presented in the paper. A supplementary online appendix is available with this article at The World Bank Economic Review website. C 2023 International Bank for Reconstruction and Development / The World Bank. Published by Oxford University Press 352 Piza et al. ing, and almost half of them were involved in hazardous activities (International Labor Organization 2020). However, recent evidence shows that the number is likely to be more than two times higher due to under-reporting (Lichand and Wolf 2022). In Brazil, more than 2.2 million, or 18 percent, of children aged 14 to 17 are economically active. Among those children, 1.2 million have paid or unpaid jobs and 80 percent of those are in the informal sector.1 Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 Bans on child labor in the form of minimum working ages are common to many countries and there has been a concerted effort by the ILO to establish a world standard minimum age of 15. The effective- ness of these bans has been questioned, mostly due to a lack of institutional capacity to enforce them in countries where child labor is prevalent and several papers finds little evidence to suggest they work or have long-run effects (Moehling 1999; Edmonds and Shrestha 2012; Bharadwaj, Lakdawala, and Li 2020; Fagernäs 2014; Manacorda 2006; Feigenbaum and Russo 2020). In this context, this paper seeks to contribute to the knowledge of the effects of labor restrictions. To do so, we use the 1998 increase in minimum employment age from 14 to 16 in Brazil as a natural experiment. In that year, more than one-quarter of all 14-year-olds in Brazil were economically active, and nearly 22 percent were working in paid or unpaid jobs. By preventing 14-year-olds from entering the labor force, and as compensating policies such as conditional cash-transfer programs or apprenticeship programs had not yet been imple- mented, the immediate effect of the ban was to reduce the choice-set of time allocation for the affected group. If they were forced to postpone their entrance into the labor market, they could potentially either continue to be economically active by seeking an informal job, spend more time attending school, or do neither.2 In addition, if the ban effectively prevented children from working and led to more time in school, it might be expected that the affected children would have better employment positions when older. How- ever if teen jobs have a significant vocational training component, being prevented from engaging in them might lead to lower labor-market outcomes a few years later (Alfonsi et al. 2020; Le Barbanchon, Ubfal, and Araya 2021). To assess the impact of the increase in minimum employment age in Brazil, we use repeated cross- sectional data from the Brazilian Household Survey from 1998 to 2006 and employ two regression dis- continuity designs: the traditional continuity-based approach and one that relies on the idea of a local randomization mechanism. We focus the analysis on urban boys, the cohort that is most likely to be af- fected by the ban. We find that the affected cohort of urban boys postponed their entrance into the labor market and saw paid labor drop more than 35 percent, driven primarily by a decrease in informal work. The ban also influenced their time allocation. From ages 14 to 18, the affected cohort of urban boys was significantly more likely to only attend school. Perhaps even more importantly, we find that these effects appear to linger. Four years after the ban, at age 18, the affected cohort was 20 percent less likely to be engaged in paid activities compared to the unaffected cohort. In addition, the affected cohort was more likely to be in school.3 The rest of this paper is organized as follows: we start with the related literature, then institutional setting and the intervention, empirical strategy, data, short-term results, and policy implications. 1 Pesquisa Nacional por Amostra de Domicílios Contínua (PNADC), 2020. 2 The Brazilian conditional cash-transfer program Bolsa Escola/Bolsa Família was in its pilot stage in 1999 (Glewwe and Kassouf 2012), and the Brazilian apprenticeship program was institutionalized in December 2000, two years after the child-labor law change. 3 In the long term, between 8 and 15 years after the policy change, we find no impact of the ban on labor-force participation rate, formal occupation, wage per hour, high-school completion rates, and college degrees. We report the results of this investigation in the supplementary online appendix. The World Bank Economic Review 353 2. Related Literature In their influential paper, Basu and Van (1998) discuss how bans on child labor can either increase adult wages enough to move the economy to equilibrium without child labor or can harm households if the increase in adult wages does not adequately replace the loss in household income (Ranjan 1999, 2001; Baland and Robinson 2000; Horowitz and Wang 2004; Dessy and Knowles 2008; Dessy and Pallage Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 2001).4 Doepke and Zilibotti (2005) develop a model in which a child-labor ban is endogenously determined.5 They predict that support for child-labor bans may increase over time once the bans are in place if the cost of schooling is sufficiently low and the value of child work is not too high. If these conditions are not met, child-labor policies might make families and children worse off. Evidence of the consequences of child labor has increased in the last 20 years. Tyler (2003) uses US data from the 1980s and finds that working while studying is detrimental to learning among high-school students. For Brazil, Bezerra, Kassouf, and Arends-Kuenning (2009) and Emerson and Souza (2011) show that very early entry into the labor market harms individuals’ outcomes in adult life over and above the effect on schooling, but this negative effect is reversed as youth age. Also for Brazil, Lee and Orazem (2010) find that an early entrance into the labor force coincides with premature school dropout and worse health outcomes.6 Beegle, Dehejia, and Gatti (2009) investigate the medium-term consequences of child labor on schooling, labor-market, and health outcomes in rural Vietnam and find that child labor has a negative effect on school attendance and educational attainment but a positive effect on labor-market outcomes such as paid work and earnings.7 The effect of child labor on study time seems crucial. Emerson, Ponczek, and Souza (2017) and Keane, Krutikova, and Neal (2022) find that child labor harms learning and cognitive development if it crowds out study time for selected low- and middle-income countries. Le Barbanchon, Ubfal, and Araya (2021) find positive effects of a youth employment program offered by a lottery in Uruguay. The authors assess whether working while in school smooths students’ transition into the labor market. The intervention targets 16- to 20-year-olds and randomly selects lottery winners for a part-time job in a state-owned company for 9 to 12 months. The authors find evidence that two years after the intervention, the treated youth had earnings 6 percent higher than the control group, suggesting that working while in school increased productivity. Enrollment rates after program participation were also 4 percentage points higher among the treated group, indicating that the intervention does not crowd out school investment. Much of the literature on the increase in the minimum employment age (MEA) relies on the American experience in the first decades of the last century. Moehling (1999) finds that minimum age limits had relatively little effect on the occupation choices of children and that these restrictions contributed little to the long-run decline in child labor. Lingwall (2014) also does not find evidence that these laws decreased the probability of kids being employed. However, Fagernäs (2014) finds evidence that MEA reduced child labor by 3 percentage points and that the enforcement of such laws was significantly improved in states that had laws on birth registration. In these places, the decrease in child labor reached 9 percentage points. And Manacorda (2006) finds evidence that MEA prevented children from working, as the author reports a significant increase in the probability of children working once they became eligible to do so. Feigenbaum and Russo (2020) documented a sizable effect of child labor and compulsory schooling laws on children from white households not involved in farming. The authors argue that children sub- 4 See Edmonds and Shrestha (2012) for a comprehensive discussion of the child-labor literature. Evidence from Brazil suggests that there are other determining factors for child labor over and above poverty, such as parental preferences for early exposure to labor markets (Emerson and Souza 2003; Emerson and Knabb 2013, 2007, 2006). 5 In our case, even if the change in the law is endogenous, we believe our results are still valid since we compare families at the margins of the cutoff at the timing of the birth realizations. 6 Health-related outcomes include a higher probability of back problems, arthritis, and reduced stamina. 7 Beegle, Dehejia, and Gatti (2009) find a few significant effects on health outcomes. 354 Piza et al. jected to the laws were 5 to 7 percentage points less likely to work. Margo and Finegan (1996) find that combining compulsory schooling and child-labor laws significantly increased school attendance by age 14. Lleras-Muney (2002) finds that the combination of both laws increased educational attainment by 5 percent and that the effects are restricted to the lower percentiles of the education distribution, therefore decreasing education inequality by 15 percent. On the other hand, Goldin and Katz (2011) find that the Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 combination of the two laws had relatively modest effects on secondary schooling rates. We are aware of only five studies that investigate the effects of an increase in the minimum employment age in developing countries. Edmonds and Shrestha (2012), using microdata from 59 mostly low-income countries, do not find evidence that suggests an influence of such laws on child time allocation that is commensurate with the level of policy attention to promoting the regulation. Bharadwaj, Lakdawala, and Li (2020) find that the rise in the MEA in India increased child labor in the informal sector and reduced wages. They also find an increase in the participation rate of siblings aged 10 to 13, particularly girls, and a reduction in school attendance. However, in Mexico, Kozhaya and Martinez Flores (2022) find a decrease in the probability of working (16 percent) and an increase in the likelihood of being enrolled in school and that these effects persist for several years. For Brazil, Piza and Souza (2016b) and Bargain and Boutin (2021) explore the increase in the minimum employment age from 14 to 16. Piza and Souza (2016b) employ a difference-in-differences design and find evidence of a 4 percentage-point reduction in paid work among urban boys, equivalent to a decrease of one-third. This drop was mostly explained by a fall in informal work. They found no impacts on girls. Bargain and Boutin (2021) employ an RDD but find that overall the legislation did not have a measurable effect; however, they do find effects in regions characterized by stronger labor law enforcement. In states with above-median inspection rates, the authors detect a 4 percentage-point decrease in child labor.8 Lakdawala, Martınez, and Vera-Cossio (2022) is an example of innovative literature that explores the decrease in the minimum working age. The authors find evidence that a Bolivian law that lowered the MEA from 14 to 10 decreased child labor among those under 14 (whose work was newly legalized) probably due to increased perceived costs of employing young children. Evidence of the long-term consequences of child-labor laws is also very limited and mostly derived from studies using compulsory schooling as an instrumental variable to estimate returns on education (Angrist 1990; Oreopoulos 2006, 2007). Many of these studies look at the impacts of educational policies on high- school quality (Dustmann et al. 2012), high-school accountability (Deming et al. 2016), teacher quality (Chetty, Friedman, and Rockoff 2014), school choice (Lavy 2015a), and teacher pay-for-performance (Lavy 2015b). Others assess the impact of youth training or vocational education on labor-market out- comes (Card et al. 2011; Hicks et al. 2013; Hirshleifer et al. 2016; Attanasio et al. 2015; Kluve et al. 2015) or “remedying” interventions targeted at disadvantaged children (Angrist, Bettinger, and Kremer 2006). Evidence from this literature points to a positive long-term effect on educational attainment and labor-market outcomes. Our study adds new evidence to the literature by evaluating the short- and longer-term effects of an active labor-market policy aimed at young people, which acted through an under-explored channel involving the restriction of time allocation for youth. 8 The differences in the results found by Piza and Souza (2016b) and Bargain and Boutin (2021) are driven mostly by two factors. First, child-labor definition employed by Bargain and Boutin (2021) is whether “children are employed, looking for a job, active but preventing from working, or working in agriculture or construction, but excluding children who are working exclusively for self-consumption or self-production”; Piza and Souza (2016b) use paid work. Second, Bargain and Boutin (2021) exclude households in which the child is not indicated as the son or daughter of the individual listed as the head of the household and households in which the head is less than 18 years old or more than 60 years old. None of these exclusions were performed by Piza and Souza (2016b). See the supplementary online appendix to understand the differences between both papers: https://github.com/dime-worldbank/child-labor-ban-brazil. The World Bank Economic Review 355 3. Institutional Background In 1988, the Brazilian Constitution established the minimum legal age of entry into the labor market as 14. In 1990, a federal rule (The Statute of Children and Adolescents) established rights for children and youth beyond regulating the conditions of formal labor-market entry.9 Complementing the constitution, the statute is considered the legal framework for children and youth in the labor market.10 Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 From 1988 to 1998, the minimum legal working age in Brazil was 14, and individuals under 17 were prohibited from working in hazardous activities. On December 15, 1998, Constitutional Amendment n. 20 increased the minimum legal age of entry into the labor market from 14 to 16, with the exception that children under 16 could work as apprentices, although the regulations for apprenticeships were not enacted until the end of 2000.11 Individuals younger than 18 were prohibited from hazardous and night- shift work. The law became effective the following day (December 16, 1998). Children younger than 16 years old, who were already employed by the time the law passed, were not affected by the ban. The administrative data on employment, the Relação Anual de Informações Sociais (RAIS), basically a census of the formal sector in the country, suggests imperfect compliance with the implementation of this legislation. In 1999, when the law was already in place, we find 14- and 15-year-olds listed in the formal market, only about a third of whom had started working before the law was enacted and were, therefore, unaffected by the ban. Among those who started working after the ban, only 2.4 percent were hired as apprentices, one of the exceptions to the ban. Interestingly, the law mostly affected individuals who turned 14 after it was passed. Using the 1999 wave of the Brazilian Household Survey (PNAD), we find that individuals who turned 14 before the ban were three times more likely to be working in the formal sector than those who turned 14 after the law change.12 Also, according to RAIS, in 1999, among those hired after the law was enacted, more than 60 percent turned 14 before the law changed. Therefore, the statistics support the view that these two cohorts were treated differently by law enforcers, labor justice officials, and/or employers. The real motivation for raising the minimum employment age is not spelled out in the law, but the two main reasons seem to have been to postpone the age of retirement under the scheme based on time of contribution to the pension system, and to acknowledge the fact that Brazil was in the process of ratifying Convention No. 138 of the ILO, which required a minimum working age of 15.13 Therefore, the country agreed to set the minimum employment age above the usual lower secondary-leaving age, which was 14 for those who had not experienced a delay in schooling by the time the law passed.14 9 Lei do Estatuto da Criança e do Adolescente, Law n. 8069, July 13, 1990. 10 In this paper the terms “children,” “teenagers,” and “youth” are used interchangeably. 11 The apprenticeship program was created in Law n. 10.097 on December 19, 2000. Before this apprenticeship law was enacted, apprentice eligibility status was unclear. Indeed, the take-up was extremely low. As discussed in Corseuil et al. (2012) the apprenticeship program integrates the Brazilian labor legislation code (Consolidação das Leis Trabalhistas), in place since 1943, but it had a very limited scope. Official census statistics from the formal sector show that in 1998 and 1999 there were only 215 and 82 14-year-old apprentices in Brazil, respectively. If the apprenticeship program had remained an alternative for youth entering the formal labor force at age 14 in 1999, it should have had a common effect on the affected and unaffected cohorts used in our analyses. It is also important to clarify that the law of 2000 is completely independent of the pension system reform of 1998. 12 This exercise compares children who turned 14 between June 25, 1998, and December 15, 1998, with the ones who turned 14 between December 16, 1998, and June 14, 1999. In the first group, 1/30 were working in the formal sector. The ratio drops to 1/100 among the second group. 13 In Brazil, there are two retirement mechanisms: an age cutoff and the amount of time one has contributed to the pension system. Because many start working early in life, they end up retiring relatively early. With the increase in the minimum employment age, people had to postpone their entrance into the formal labor force by two years. Consequently, they would retire two years later. 14 At that time, primary and lower secondary education was mandatory in Brazil. According to Constitutional Amendment 14, in 1996, the state was required to provide public and mandatory first to eighth grades, including for those who did 356 Piza et al. The change in the minimum working age extended the existing child-labor laws to age 16, including penalties and fines associated with violating the law. Employers (including parents if the child works for a family business) who violate the law can face several forms of penalties, ranging from fines and other administrative costs, to criminal prosecution, depending on the type of work children perform. Children are not subject to any sort of penalty in either case, as the goal of the law is to protect them (Medeiros Neto Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 and Marques 2013). One might question the enforceability of such a law in a country where informal work is widespread. However, it is important to understand the distinction between formal firms (those registered with the government) and formal workers (those workers who are formally registered and have a work permit). For formal workers, the enforceability of the law is almost deterministic – though imperfect as suggested by official statistics – given that the Ministry of Labor is the institution responsible for issuing work permits. With the change in the law, the ministry should not have issued work permits to individuals who turned 14 after the ban.15 However, since only 1.5 percent of 14-year-olds were working formally in 1999, we expect the effect of the ban to be very small among this group.16 However, it is quite common for formal firms to employ informal workers. In his study of formal firms, Ulyssea (2018) suggests that around 40 to 50 percent of all workers in formal firms are informal. Data from Almeida and Carneiro (2012) show that inspections of formal firms often uncover informal workers, and that annually, about 20 percent of all formal firms in Brazil are inspected. Firms in Brazil are subject to routine inspection by the Ministry of Labor and Employment (MTE), under the aegis of the Secretary of Work Inspection (SIT). These inspections are coordinated and tracked by the Federal System of Labor Inspection (SFIT). In addition, in 1998, the Public Ministry of Work (MPT) also began to conduct inspections alongside the SIT. Abras et al. (2018) find that most inspections are triggered by anonymous reports. As child labor can be quite visible (children are easily identified by their appearance), there is a strong likelihood that shedding child labor is not just due to the outcome of an actual inspection, but also done pre-emptively by firms that wish to avoid formal inspections. Since formal firms generally employ a lot of informal workers, inspections can be very costly, not just due to fines for employing children, but also from the fines as well as the back taxes for informal workers found during inspections. There are also increased ongoing costs associated with having to register informal workers as formal workers. Additionally, as all Brazilians are issued a national identity card that identifies their age, it is quite easy for firms to know the true age of workers. For these reasons it is reasonable to expect a large impact on informal child labor from the ban through formal firms and that the precise age cutoff is a binding constraint.17 The compulsory schooling law could be seen as a confounding factor for our identification strategy. The birthdate cutoff adopted by the school system to determine that a seven-year-old child can enroll in school in a given year can create a discontinuity around the cutoff used to identify the effects of the child- labor ban. If school enrollment and attendance are no longer mandatory for the children who turned 14 before the increase in the minimum working age but remain mandatory for those who turned 14 after, not attend school at the correct age for the grade. With delay common in Brazil, this law affects many older children who have not yet completed eighth grade. 15 Except for apprenticeship contracts, allowed by the law. These employees have the labor contract recorded on the worker register card. 16 PNAD, 1999. 17 The results found by Piza and Souza (2016b) support this conclusion. They find a decrease in informal paid work among boys in urban areas, suggesting that some employers decided to stop employing children under the age of 16 to avoid legal consequences as mentioned above. Another possible interpretation is that the ban reduced labor demand through increased adult wages, consistent with the theoretical predictions in Basu (2005). (Bharadwaj, Lakdawala, and Li (2020) interpret the increase in the minimum legal age in India along the same lines. We thank an anonymous referee for pointing out this commonality.) The World Bank Economic Review 357 the discontinuity observed around the cutoff could not be fully attributable to the child-labor ban. This would not invalidate the exogeneity of the discontinuity, but the results could not be interpreted as being exclusively a consequence of the child-labor ban. As we argue in the results section, we are confident that the discontinuity we observe is due to the child- labor ban. First, educational delay in Brazil is very common and students must stay in school until they Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 complete lower secondary education. Since delays were pervasive at the time the law changed, only 3.3 percent of the 14-year-olds were no longer obliged to stay in school.18 Second, the school system in Brazil is highly decentralized, and each local district uses different cutoff birth dates to allow the enrollment of students in the first grade. Finally, a series of placebo tests using affected and unaffected cohorts do not reveal discontinuities in the outcomes of interest. 4. Empirical Strategy Our identification strategy relies on the children’s dates of birth, since the change in the minimum legal working age on December 15, 1998, affected those who turned 14 after this date. Unlike Angrist and Krueger (1991) and many other authors who combine date of birth with school entry or exit ages, parents could not have anticipated this change or its effects.19 Since the law affected those children who had their 14th birthday just before the cutoff differently from those whose 14th birthday fell just after it, the regression discontinuity approach is the most appropriate for our analysis. We use two inference approaches of regression discontinuity design (RDD) to examine the effect of the ban on the outcomes of those the law impacted. The first utilizes a continuity-based approach and the second relies on the idea of local randomization, in which the treatment assignment is regarded as a known randomization mechanism near the threshold (Cattaneo, Titiunik, and Vazquez-Bare 2016). We use two inference approaches of regression discontinuity design (RDD) to examine the effect of the ban on the outcomes of those the law impacted. The first utilizes a continuity-based approach and the second relies on the idea of local randomization, in which the treatment assignment is regarded as a known randomization mechanism near the threshold (Cattaneo, Titiunik, and Vazquez-Bare 2016).The cutoff, Z¯ , is set on December 16, 1984, that is, 14 years before the law started being applied. The running variable, Zi , is the number of weeks between the cutoff and date of birth of child i. Therefore, Zi = 0 if child i was born on the cutoff date or up to one week after that, Zi = 1 if child i was born between one and two weeks after Z ¯ , Zi = 2 between two and three weeks after Z ¯ , and so on. Analogously, Zi = −1 ¯ if child i was born up to one week before Z, Zi = −2 for between one and two weeks before, and so on. The affected cohort, Di = 1, is set when Zi ≥ 0, and the unaffected cohort, Di = 0, when Zi < 0. Our empirical strategy leverages the discontinuity around the age cutoff points to estimate treatment effects using an RDD. We start with the continuity-based approach, that is, the standard RDD which relies on the continuous distribution of both the running variable and pre-treatment covariates around the threshold. For a small enough bandwidth size, treatment and control groups are expected to be statistically similar, on average, in both observed and unobserved characteristics. We employ a non-parametric method to fit local linear regressions on each side of the cutoff point (see Calonico, Cattaneo, and Titiunik 2014a,b) as illustrated by the regression equation below: yi = α + γ Di + θ0 Zi + θ1 Di Zi + υi , where yi is the outcome of interest of child i, Dic is an indicator function that assumes the value of 1 if Zi ≥ 0, Zi is the running variable defined as before, and υ i is the error term. This approach relies on extrapolation and large-sample approximations of the conditional expectation using observations on each 18 PNAD, 1999. 19 For similar identification strategies see Smith (2009), McCrary and Royer (2011), Black, Devereux, and Salvanes (2011), Oreopoulos (2006), Dickens, Riley, and Wilkinson (2014), Lavy (2015a, b). 358 Piza et al. side of the cutoff. Our benchmark specification uses a uniform kernel and the conventional bias-correction approach. Given the key role played by the bandwidth size in the regression discontinuity estimates, we use differ- ent mean square error minimization methods to select the optimal bandwidth size (Calonico, Cattaneo, and Titiunik 2014b; Imbens and Kalyanaraman 2012). The optimal bandwidth is 14 weeks. Because the Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 selection of the optimal bandwidth does not take statistical power into account and inference relies on asymptotic distributions, we report estimates with 26 and 39 week bandwidth as well.20 The empirical appeal of RDD is that estimates close to the cutoff point should be as good as if the treatment assignment had been random. However, RD users face a trade-off between bias and variance as in many applications sample size near the threshold is not sufficiently large to allow for very local inference with enough precision. To claim a local treatment assignment in RD applications, estimates need to be obtained with a very narrow bandwidth size. In practice, that would require an inference method that works with small sample sizes, and does not rely on the specification of the running variable. This is exactly what the local randomization mechanism does (Cattaneo, Titiunik, and Vazquez-Bare 2016). In our case, it is the same as assuming that turning age 14 just before or after the law change is random. Moreover, different from the continuity-based approach, the local randomization procedure does not rely on infinite extrapolation assumptions and asymptotic distributions. Instead, it applies a finite-sample exact inference method (randomization inference), something ideal when the sample size used for inference is small, as it is in our case. To define the window around the cutoff where the local randomization is assumed to hold, we follow the data-driven method proposed by Cattaneo, Titiunik, and Vazquez-Bare (2016). Since the methodology assumes the treatment is random inside a window around the cutoff, W0 = [Z ¯ + w], w > 0, the ¯ − w, Z distribution of pre-intervention characteristics or post-intervention unaffected outcomes should be the same, on average, between the affected and unaffected cohorts inside W0 . On the other hand, for the procedure to be useful, the distribution of these covariates should be unbalanced outside the optimal window.21 To understand this in our context, consider two (k = 2) covariates that are unaffected by the treatment: mother’s years of schooling (x1it ) and household size (x2it ) in year t = 1999, for which we run the following regression equation: xkit = α + β Di + υi , k = 1, 2, t = 1999. The window-selection algorithm consists of finding the largest window (W0 ) in which the p-value for the null hypothesis of no effect of the treatment (H0 : β = 0) is always larger than some pre-specified level, for example, 0.15. Therefore, inside the determined window, we should not observe a p-value lower than 0.15. If we do, it means the window size is too wide. A smaller window size is then proposed and the balance test is rerun. The simulation stops only when one cannot observe any p-value in the balance test exercise below 0.15 inside a given window. Performing this data-driven process on our sample resulted in a 14-week bandwidth around the cutoff.22 Given that a 14-week window size might be considered relatively large in a framework reliant on a local randomization design, we focus on the estimates with a 10-week bandwidth.23 20 To check robustness, Imbens and Kalyanaraman (2012) recommend using both half and double the optimal bandwidth to check robustness. In tables S2.2 and S2.3 we show results with various window sizes. 21 We run a test of difference in means and the p-values are calculated according to Fisherian inference as in Cattaneo, Titiunik, and Vazquez-Bare (2016). 22 The variables used to select the bandwidth are the mother’s education, head of household’s education, head of house- hold’s age, and household size. Figure S3.1 in the supplementary online appendix depicts the p-values by window length. 23 This method accommodates adding polynomials of the running variable in the specification. In these cases, the local randomization method loses its appeal, as controlling for the running variable weakens the method’s rationale. The World Bank Economic Review 359 Hence, the analysis of the short- and longer-term effects of the law on individual outcomes consists of comparing the cohorts who turned 14 years old up to 10 weeks before the law changed (born between October 6, 1984, and December 15, 1984) with those who turned 14 up to 10 weeks after the law changed (born between December 16, 1984, and February 23, 1985). If the increase in the minimum employment age led to a change in labor-force participation and employment, then the outcomes of the Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 unaffected cohort would inform what would have happened to those hindered from working had the law not changed. To assess the short-term effects of the law and its persistence over time, we follow the affected and unaffected cohorts from age 14 to age 21. We use labor-force participation, the incidence of children working for pay (formal and informal), the incidence of children attending school, and the incidence of children only attending school. Therefore, we aim to examine whether the law significantly reduced the share of children working for pay and whether those prevented from working opted to postpone their entrance into the labor market, continue looking for a job (still in the workforce, but unemployed), or were more likely to continue going to school. By looking at the 2001 data, we can check whether the law had an impact on the affected cohort’s likelihood of being employed after reaching the minimum legal working age of 16. If the ban prevented children who would have chosen to work from doing so at ages 14 and 15, it might be reasonable to expect that, once they turn 16, they would then enter the labor market and thus we would not observe persistent effects of the ban at ages beyond the affected ones. There are a few reasons why we might expect effects at older ages. First, if the choice to work was optimal at age 14, it might no longer be so at age 16 as the choice set has now changed, particularly if the intervening two years were spent in full-time school and are, at age 16, a sunk cost. The new optimal decision might be to continue until the award of the high-school diploma rather than work. There could also be a bounded rationality effect, where the information gleaned in the extra two years of education reveals more about the true returns which could also lead to choosing more education at 16. Finally, there could be a cost, a “scarring effect,” to being forced out of the labor market at 14, where they could lose out on the experience and vocational training, which is not compensated by the extra schooling – perhaps due to the poor quality of Brazilian public schools.24 5. Data We use several years of the Brazilian household survey (PNAD), which was conducted annually from the late 1970s to 2015 by the Brazilian Institute of Geography and Statistics (IBGE).25 The year 1998 is used for placebo tests and data on child-labor characteristics before the change in the minimum legal working age. The year 1999 is used for descriptive statistics for affected and unaffected cohorts and short-term estimates. We then use PNADs from 2001 to 2006 to assess the persistence of short-term effects.26 Generally conducted in the last week of September, the PNAD interviews about 380,000 individu- als in around 100,000 households.27 The survey is nationally representative and constitutes one of the main sources of microdata in Brazil. It contains information on household socioeconomic characteristics, demographic data, educational attainment, household sources of income, and labor-force status. Our sample consists of two cohorts of individuals who were 13 or 14 years old at the time of the increase in the minimum legal working age. The first cohort, defined as the affected group, consists of individuals who turned 14 after that. The second cohort, which we consider the comparison group, in- cludes individuals who turned 14 before December 16, 1998, the first day the law was applied. In the 24 Supplementary online appendix S1 discusses the long-term estimates (from 22 to 29 years old). 25 IBGE stands for Instituto Brasileiro de Geografia e Estatística. 26 There was no PNAD in 2000 due to the national census. 27 Average between 1998 and 2014. 360 Piza et al. continuity-based approach, our baseline specification has a 9-month bandwidth (table S2.1). For the lo- cal randomization approach, our baseline is a 10-week bandwidth.28 From the PNAD, we create six variables of interest.29 Economically active assumes value 1 if the person is employed or unemployed and 0 if the person is out of the labor market.30 Paid work assumes value 1 for those employed for a wage and 0 otherwise. The paid work category is also divided between those working Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 in the formal sector, Formal paid work, and the informal sector, Informal paid work. The employees are considered formal if their labor identification document is signed by their employer guaranteeing the labor rights established by the Brazilian legislation, such as paid vacations, contribution to social security, unemployment insurance, and sick leave, among others.31 Attending school assumes value 1 for children who attend school and 0 otherwise. Only attending school assumes value 1 for children who only attend school and 0 otherwise. We then multiply all the outcomes by 100 so the estimates can be interpreted in percentage points. 5.1. Descriptive Statistics We begin by introducing descriptive statistics for child labor in Brazil in 1998, immediately before the increase in the minimum legal working age. We provide a framework for boys and girls in both urban and rural areas for context, before focusing on boys in urban areas for whom the ban had a measurable impact. In 1998, 26.7 percent of all 14-year-olds were economically active, and 22 percent were working, either in paid or unpaid jobs (fig. S3.2). Their unemployment rate was 18 percent, more than twice as high as that of 18- to 65-year-olds. Ninety percent of these children were enrolled in school, with almost 97 percent in lower primary or upper primary education, meaning they still had not completed the mandatory level of education.32 Among the children working, 81.4 percent combined work and school and 56 percent were in unpaid activities.33 In rural areas, 47 percent of 14-year-olds were working in 1998. Among those working, 80 percent were unpaid and 98.2 percent of them were either members of the household in which they worked or were workers for self-consumption/production. In urban areas, 14 percent of 14-year-olds were working in 1998, with boys twice as likely to work as girls. When working, three-quarters of girls were engaged 28 We used the Stata command rdwinseled proposed by Cattaneo, Titiunik, and Vazquez-Bare (2016) to estimate the optimal bandwidth. The procedure suggests a 14-week bandwidth. Conservatively, we show the results for 10, which we consider the baseline, and 14. 29 See the code in https://github.com/worldbank/child- labor- ban- brazil. 30 The IBGE defines as employed people that worked in the reference week of the survey (if V9001 = 1), that worked for self-consumption (if V9002 = 2) or self-production (V9003 = 1), or that had a paid job but were on leave in the reference week (V9004 = 2). Therefore, the variable employed is equal to 1 if V9001 = 1 or V9003 == 1 or V9002 = 2 or V9004 == 2 and 0 if the person was not working but did look for a job in the reference week of the survey (V9115 = 1). The unemployed are those who were not working in the reference week but did look for a job (if V4705 = 2). Therefore, unemployed is equal to 1 if employed is equal to 0, and is equal to 0 if employed is equal to 1. In the 1999 PNAD wave, the IBGE set up the variable V4704 as equal to 1 for those economically active and equal to 2 for those out of the labor market. All the variables mentioned are in the 1999 PNAD wave. 31 Civil servants (V4706 = 2 or V4706 = 3) are also considered formal employees, as well as those people that, even though they do not have a signed labor card, pay pension contributions to the National Institute of Social Security (Instituto Nacional de Seguridade Social, INSS) (V4711 = 1). Therefore, formal paid work assumes a value of 1 for those employed with a signed labor card, for civil servants, and for employees that contribute to pensions, and 0 otherwise. Informal paid work assumes value 1 when formal paid work is 0 and 0 when formal paid work is 1. 32 In Brazil the education system is divided into the following categories: Pré-escola (4- to 5-years-old), Fundamental I (6- to 10-years-old) which we call primary, Fundamental II (11- to 14-years-old) which we call lower secondary, and Ensino Médio (15- to 17-years-old) which we call upper secondary. Schooling is mandatory through Fundamental II. 33 PNAD, 1998 wave. Check our replication package to reproduce the descriptive statistics: https://github.com/worldbank/ child- labor- ban- brazil. The World Bank Economic Review 361 in paid activities, for an average of 35 hours per week. More than half of them worked as housekeepers, the vast majority in their employer’s household, where labor-law enforcement is limited or nonexistent. None of these girls worked in the formal sector. Among boys working, two-thirds were in paid jobs in factories, services, or offices, where inspection might occur more frequently, although only 1 percent were in formal sector jobs. Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 In households with 14-year-old children, 5 percent of the total household income came from the wages of individuals up to 17 years old. In 10 percent of these households, more than 20 percent of the income came from children’s wages.34 This indicates that the effects of the ban might vary according to the socioeconomic level of the families, as some households rely more on these resources than others. With the overall context of child labor in Brazil clear, we now turn our attention to the subjects of this study: boys in urban areas, the ones most likely to be affected by the ban. Between 1999 and 2005, we observe a steady increase in the percentage of urban boys who work for pay, but there is a significant gap between those unaffected by the ban and the affected cohort. In 1999, the difference between affected and unaffected cohorts working for pay was 5.4 percentage points. The gap increased to more than 6 percentage points in 2001 and 2002 and reached more than 10 percentage points in 2003 when the cohorts were 18 years old. The gap starts decreasing at 19 years old (fig. S3.3). The increasing gap in working for pay was accompanied by a gap in labor-force participation, which might indicate that the affected cohort postponed their entrance into the labor market. In addition, al- though we see a significant decrease in school attendance for both cohorts, more than one-third were still in school by age 19. Since by this age, most of them should have graduated from high school, we might expect to see them in college; however, only 26.9 percent were attending a university. Of 19-year-olds in school, 12.5 percent were still enrolled in lower secondary education, and roughly 40 percent were in high school, suggesting significant school delay.35 5.2. Visual Check To determine whether the child-labor ban affected school attendance, children’s employment, and labor- force participation, we compare the affected and unaffected cohorts using the 1999 PNAD. There is evidence that the law was enforced. For a 14-week bandwidth, the percentage of 14-year-olds in paid activities is 5.4 percentage points smaller among the affected cohort (fig. S3.4). One may wonder whether this cohort, though legally prevented from working, continued looking for a job. This does not seem to be the case, as the percentage of economically active children is 5.7 percentage points smaller for the affected cohort (fig. S3.4). We further inspect this relationship using local linear regressions. We run non-parametric regressions on each side of the cutoff point for the following outcomes: economically active, paid work, informal paid work, and children only attending school. These four outcomes are the main ones in which we expect short-term impacts of the ban. We estimate the local linear regressions using a triangle kernel with a 14-week bandwidth, and a 4- week bin size. Figure 1 suggests that the decrease in the proportion of children working for pay was mainly driven by those combining paid work with schooling. Overall, the visual analyses suggest some children traded work for education, while others decided to keep working in the informal sector. 5.3. The Plausibility of the Identification Assumption The identification strategy used in this paper assumes that turning 14 by the time of the increase in the minimum working age can be defined as a known randomization mechanism around the cutoff. Although our birth data come from household surveys conducted by the Brazilian Census Bureau, which is not 34 PNAD, 1998 wave. 35 There were 2.4 percent enrolled in primary education – 2004 PNAD wave. 362 Piza et al. Figure 1. Visual Check, Urban Boys (1999). Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 Source: 1999 wave of the Brazilian Household Survey (Pesquisa Nacional por Amostra de Domicílios – PNAD). Note: The figures show local linear regressions fitted on each side of the cutoff point. We use a 4-week bin size and a triangle kernel with 12-month bandwidth on the sample of 14-year-old urban boys. related to the public institutions responsible for the surveillance and enforcement of the law, there is the possibility that families misreport the dates of birth of their children, particularly in cases where they are working illegally. If this occurs systematically, one would observe a discontinuity in the density function of the forcing variable around the cutoff point, which would call into question the plausibility of our identification strategy. We do not think that manipulation is an issue of concern in our setting, because Brazil’s Ministry of Labor, responsible for issuing work permits, requires an individual’s birth certificate or other official identification. Even so, we perform a McCrary density test to investigate whether there is any indication of manipulation. The test consists of comparing the density distributions of the forcing variable around the cutoff point (McCrary 2008).36 A rejection of the null hypothesis would indicate perfect manipulation of the forcing variable. Figure S3.5 illustrates the results graphically and indicates that there was no perfect manipulation of the forcing variable. 36 Because household heads or responsible adults report the ages of household members to the surveyor, misreporting or manipulation is possible. It is important to emphasize that RDD accommodates some degree of sorting or manipulation of the forcing variable. To invalidate the identification strategy, a perfect manipulation of the forcing variable should be observed. See Lee and Lemieux (2010) for a discussion. The World Bank Economic Review 363 Table 1. Local Polynomial Regression Discontinuity, Boys in Urban Areas (1999) Economically active Paid work 14 weeksa 26 weeks 39 weeks 14 weeks 26 weeks 39 weeks RD estimate −4.3 −3.9 −6.86∗∗ −1.86 −4.10∗ −5.46∗∗∗ Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 Standard error (7.07) (4.37) (3.26) (3.28) (2.32) (1.86) Obs 1,576 2,962 4,431 1,576 2,962 4,431 Formal paid work Informal paid work 14 weeks 26 weeks 39 weeks 14 weeks 26 weeks 39 weeks RD estimate −0.5 −0.97∗∗ −0.34 −1.36 −3.12 −5.12∗∗∗ Standard error (0.63) (0.45) (0.42) (3.41) (2.39) (1.92) Obs 1,576 2,962 4,431 1,576 2,962 4,431 Attending school Only attending school 14 weeks 26 weeks 39 weeks 14 weeks 26 weeks 39 weeks RD estimate 1.3 3.93 2.68 6.24 5.58 7.38∗∗ Standard error (3.61) (2.56) (1.99) (7.83) (4.84) (3.44) Obs 1,576 2,962 4,431 1,576 2,962 4,431 Source: 1999 wave of the Brazilian Household Survey (Pesquisa Nacional por Amostra de Domicílios – PNAD). Note: Authors’ estimate. Conventional regression-discontinuity-design estimates as proposed by Calonico et al. (2017). The running variable is the number of weeks between the date of birth and the cutoff (December 16, 1984). No covariates. Uniform kernel. Tables S2.2 and S2.3 show the Romano–Wolf stepdown p-values for multiple hypothesis testing following Clarke (2021). Tables S2.4 and S2.5 show robustness checks using the 1998 wave of the Brazilian Household Survey. a Regression Discontinuity Design bandwidth in weeks. ∗∗∗ , ∗∗ , and ∗ indicate significance at the 1, 5, and 10 percent critical levels. The validity of our identification strategy also requires a smooth distribution of observed characteristics of 14-year-olds around the cutoff. Under the assumption that the law gave rise to a natural experiment, we should observe affected and unaffected cohorts with similar observed characteristics, on average. For balance in observed characteristics, we use covariates usually employed in labor supply estimates: parents’ age and education, household size, self-reported skin color, and urban or rural areas, and check whether they are smoothly distributed around the cutoff point. We find no systematic differences in the mean values of these variables between unaffected and affected cohorts (table S2.1). 6. Short-Term Effects of the Ban To assess the effects of the increase in the minimum legal working age from 14 to 16 years old, we first estimate the treatment effects using the continuity-based approach. Table 1 shows the estimates for the sample of boys in urban areas using 14-week, 26-week, and 39-week bandwidths. The signs and magnitudes of the point estimates of all three different bandwidths are similar. We find evidence of a significant decrease in the number of boys who are economically active, who are in paid work, and who are in informal paid work, and we also find an increase in boys only attending school for the 39-week bandwidth.37 The estimates suggest that the change in minimum working age led to a decrease in paid work of at least 5.5 percentage points among the affected urban boys impacted by the ban, a drop of 35 percent.38 The results suggest that it is the decrease in informal paid labor that seems to be driving this result. This may seem counterintuitive as the ban might be expected to impact formal workers more 37 This suggests that the statistically insignificant results from the other bandwidths are mainly due to the lack of power. 38 One may argue that the decrease in child labor might be driven by under-reporting. However, we do not believe that this is the case. First, the information the household provides to the IBGE enumerator is not shared with the Ministry of Labor, the authority that is in charge of monitoring compliance with the law. Second, the fact that the effects persist 364 Piza et al. Table 2. Local Randomization, Boys in Urban Areas 10 weeks (RDD bandwidth) 14 weeks (RDD bandwidth) ATEa 95% CIb Meanc ATEd Obse ATE 95% CI Mean ATE Obs outcome as % outcome as % Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 Economically active − 6.65∗∗ [−11., −1.1] 28.5 − 23.3 1,067 − 7.84∗∗∗ [−12., −3.3] 29.9 − 26.2 1,531 Paid work − 5.23∗∗∗ [−9.3, −1.4] 14.9 − 35.1 1,067 − 6.68∗∗∗ [−9.9, −3.3] 15.7 − 42.6 1,531 Formal work − .541 [−1.4,.37] 0.6 — 1,067 − .771 [−1.5, −1.1] 0.9 — 1,531 Informal work − 4.68∗∗ [−8.2, −.93] 14.3 − 32.8 1,067 − 5.91∗∗∗ [−9.1, −2.8] 14.8 − 39.9 1,531 Attending school 3.671∗∗ [.37,7.1] 89.9 4.1 1,067 3.897∗∗∗ [1.0,6.5] 90.5 4.3 1,531 Only attending school 7.996∗∗∗ [2.6,12.] 71.7 11.2 1,067 8.392∗∗∗ [4.1,12.] 71.5 11.7 1,531 Source: 1999 wave of the Brazilian Household Survey (Pesquisa Nacional por Amostra de Domicílios – PNAD). than informal due to enforcement issues, but the result is likely due to the fact that much of the work done by urban boys is in formal firms, but as informal labor and/or in informal activities more visible to the public and inspectors such as commerce and services. So formal firms with children engaging in more visible activities, which could be subject to inspection, might have a strong incentive to shed their informal child labor. As a robustness check, we estimate the same model on the same cohort of urban boys, but in the 1998 PNAD when they were 13 years old. As the ban had not been implemented when the cohort was 13, we do not expect to see significant differences in outcomes due to the law. Table S2.6 shows the placebo results, and they are as expected: there are no significant differences between the groups before the increase of the minimum employment age for any of the outcomes of interest across all of the bandwidths, which is strong evidence that the effects we estimate using the 1999 PNAD are due to the change in minimum working age. Given the lack of precision in the standard RD regressions with smaller bandwidth sizes, we also present the results from the model which assumes a local randomization mechanism. Local randomization is ideal in our setting as inference of local estimates can be carried out with small samples around the threshold and is fully non-parametric. We use the data-driven method proposed by Cattaneo, Titiunik, and Vazquez- Bare (2016) to select the bandwidth size consistent with the assumption that treatment assignment was “as if random” near the cutoff point. The method selected 14 weeks as the optimal bandwidth. Because the method estimates treatment effects using a simple difference in means – as one would do if treatment assignment was random – we narrow it down to 10 weeks to make the “random assignment” mechanism more credible in our context. Table 2 shows the results for urban boys in the 1999 PNAD with the two bandwidth sizes. For the most part, the estimates are very consistent with the results in table 1. Among those economically active, we estimate a decrease of 6.65 percentage points, which corresponds to a drop of more than 20 percent. Among those in paid work, we estimate a decrease of 5.23 percentage points, which corresponds to a drop of at least 35 percent. The decrease in informal paid work remains the largest component of the overall effect with a reduction of almost 33 percent. The estimates also show an increase in school attendance of almost 4 percentage points, and the share of those only attending school increased by around 8 percentage points, indicating that the affected group of boys opted to return to school or continue attending school, instead of opting to neither work nor go to school. The change in the minimum working age does not appear to have had a significant impact on unpaid work. This is not surprising as 95 percent of 14-year-old boys in urban areas working in unpaid activities were either working for self-consumption or were a member of the household for which they worked, even after the affected cohort is legally allowed to work suggests that the impacts found are not being driven by under- reporting. The World Bank Economic Review 365 suggesting that the enforcement of the ban might not affect them. Also, the results of a decrease in paid labor and an increase in only attending school are driven mainly by the decrease in those working and attending school, thus suggesting that the schools might play an additional role in law enforcement. In fact, schools have to report the students’ attendance to the authorities regularly, which might lead to enforcement actions. Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 6.1. Robustness Check of Local Randomization Results Table 2 shows the local randomization results for the “optimal” 14-week bandwidth and a more con- servative bandwidth of 10 weeks. To ensure these results are robust to different windows around the cutoff, we run a robustness check proposed by Cattaneo, Titiunik, and Vazquez-Bare (2016). We then test whether the results are robust considering a bandwidth range between 10 and 18 weeks. In this exercise, instead of testing H0 : ATE = 0 versus ATE = 0, we test H0 : ATE = γ , with γ = 0, versus H1 : ATE = γ . Hence, we have evidence that the results are robust if we do not reject the null hypothesis over the range of all bandwidths tested. Figure S3.6 shows the average treatment effects under the null hypothesis on the y-axis and the number of weeks around the cutoff on the x-axis (10–18). The figure also shows the p-values for several tests. For all six outcomes under evaluation, the p-values are higher than 0.3 and, therefore, we do not reject the null hypothesis. 6.2. Persistence of Short-Term Effects Once they reach the age of 16, children are no longer banned from working. If the forces that would have caused them to work in the previous two years have not changed, it might be expected that there would be no persistent effect of the ban. However, there are some reasons to expect more lasting effects. One could be that there is a “scarring effect,” that by leaving the labor force it is actually harder to return than if entering for the first time, and thus it takes longer for them to get back. Information might also be important, families might learn more about the returns to education and the child’s ability in school once the child returns to school full time. The optimal decision is also different at 16 and after being excluded from working for two years: the decision to invest in a high-school diploma at 14 might not make sense as the opportunity cost is too high. But taking away the option of earning a wage at 14 and directing kids to school might change the calculation. It might now be optimal to continue to invest in school, especially as they are close to the bump in expected returns that come with the credential of a high-school diploma. In fact, there is evidence of persistent effects in a different context. In their recent evaluation of a child-labor ban in Mexico, okk (Kozhaya and Martinez Flores 2022) find lasting effects, which suggests that there might be similar dynamics in Brazil. To test whether the estimated effects of the ban continue even after the boys reach age 16 and be- yond, we explore their persistence by following the affected and unaffected cohorts from 1998, one year before the ban, when they were 13 years old, to 2006, when they turned 21. We also employ the local randomization approach since it allows us to investigate this question without relying on parametric as- sumptions and extrapolations when using cross-sectional data. Figure 2 shows the point estimates with a conservative bandwidth size of 10 weeks and a 95 percent confidence interval. The results indicate that the reduction in economic activity is seen at ages 17 and 19, the reduction in paid work persists through ages 16 to 18, and the reduction in informal work is measurable at age 17. During this period, the affected cohort was nearly 20 percent less likely to be engaged in paid work than the unaffected one. We observe that the affected cohort became economically active when they reached the minimum employment age (16) and were legally allowed to work. However, being less likely to find a paid job might have discouraged them from looking for a job as the difference in the percentage of those economically active became significant again when the cohorts turned 17. One year later, these 18-year- olds seemed to have returned to the economically active population but they appeared to face challenges 366 Piza et al. Figure 2. Persistence of Short-Term Effects of the Ban, Boys in Urban Areas (10-Week Bandwidth). Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 Source: 1998 to 2006 waves of the Brazilian Household Survey (Pesquisa Nacional por Amostra de Domicílios – PNAD). Note: Authors’ estimate. Local randomization in which the running variable is the number of weeks between the date of birth and the cutoff (December 16, 1984). We employed the Stata command rdrandinf proposed by Cattaneo, Titiunik, and Vazquez-Bare (2016). Constant effect model (polynomial of order 0). Ten-week bandwidth. We followed the affected and unaffected cohorts from 1998 to 2006, that is, from 13 to 21 years old. The y-axis shows the average treatment effects in percentage points. engaging in paid activities. On the other hand, we see a significant increase in those attending school at 18 and those only attending school at ages 17 and 18.39 The challenges faced in getting a job might be due to the lack of experience that seems to have surpassed the benefits of the availability of more hours a day to engage in academic activities. In fact, more than 95 percent of the affected cohort were enrolled in public schools, the majority of them known for the low quality of their education.40 The postponement of entry into the labor market and the consequent increase in the percentage of youth only attending school did not lead to a significant difference in acquiring a high-school diploma. Indeed, when affected and unaffected cohorts turned 19 and should have finished this level of education, there is no significant difference in the percentage of the groups with a high-school degree (39.7 percent and 41.1 percent, respectively).41 The result suggests that the unaffected group, despite being more likely to have a paid job, did not stop attending school. There were no significant differences in school attendance when the cohorts were 16 and 17. 39 The fact that the effects seem to increase at 18 and 19 for some results might be an artifact of the fact that at 18 individuals can work in all activities, including hazardous work, so the supply of workers might increase, leading to larger relative impacts. 40 According to the 2003 Programme for International Student Assessment (PISA), among 40 countries, 15-year-olds in Brazil had the lowest proficiency score in math, the second-lowest score in science, and the lowest-worst score in lan- guage. 41 PNAD, 2004 wave. Sample of urban boys with a 10-week bandwidth around the cutoff. The World Bank Economic Review 367 7. Discussion and Policy Implications On December 15, 1998, the minimum employment age in Brazil changed from 14 to 16 years old and was applied the following day. The law appears to have had an immediate impact on 14-year-old urban boys who postponed their entrance into the labor market. This coincided with an increase in attending school only among this group between ages 14 and 18. Disappointingly, this increase in schooling did not Downloaded from https://academic.oup.com/wber/article/38/2/351/7381104 by Sectoral Library Rm MC-C3-220 user on 01 May 2024 lead to a higher percentage of boys getting a high-school degree. This appears to be due to the high degree of dropout between lower secondary and upper secondary education – only 40 percent of the studied cohorts had a secondary-school degree at 19 years old. Interestingly, the cohort unaffected by the ban was not less likely to be attending school at 16 and 17 years old, suggesting that those who worked were successful in combining work and school. The affected cohort was able to join the working population at age 16, but they continued to be less likely to get a paying job. Indeed, four years after the ban, at age 18, they were almost 20 percent less likely to be engaged in paid activities than the unaffected cohort. The difficulty in finding a job opportunity might have discouraged them from continuing to look for a job, as there are significant differences in the percentage of those economically active when boys turned 17 and 19. The challenges these boys faced in getting a job opportunity might be due to the lack of previous experience, imposing barriers later on. On-the-job experience seems to have surpassed the benefits of the availability of more hours a day to engage in academic activities. It seems likely that the muted effect of the ban was not due to its lack of effectiveness, but to the poor quality of the schools that served the affected population. Despite those challenges, the affected boys do not seem to have started with lower wages when compared to the unaffected ones. We find that the child-labor ban adopted in Brazil was successful in reducing child labor as intended. The increase in the minimum working age, aimed to delay entry into work, had a measurable effect on labor-force participation and employment. Children prevented from working appear to have concentrated their time on attending school. However, the potential benefits of this change seemed to be constrained by problems in the education system that served them: a combination of school dropout, low-quality educa- tion, and lack of compensating outside options such as vocational training and apprenticeship programs. Together, these effects suggest that it might not be enough to enact policies that limit the work of children but might be equally important, in tandem, to improve the quality of public education. It might also be important to allow formal part-time jobs with a strong vocational component, where children can gain skills required by the adult labor market. 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