Child Labor Bans, Employment, and School Attendance: Evidence from Changes in the Minimum Working Age

Abstract

This paper investigates the effect of a unique child labor ban regulation on employment and school enrollment. The ban, implemented in Mexico in 2015, increased the minimum working age from 14 to 15, introduced restrictions to employing underage individuals, and imposed stricter penalties for violation of the law. Our identification strategy relies on a DiD approach that exploits the date of birth as a natural cutoff to assign individuals into treatment and control groups. The ban led to a decrease in the probability to work by 1.2 percentage points, resembling a 16 percent decrease in the probability to work relative to the pre-reform mean, and an increase in the probability of being enrolled in school by 2.2 percentage points for the treatment group. These results are driven by a reduction in employment in paid work, and in the manufacturing and services sectors. The effects are persistent several years after the ban.

1 Introduction

From 2012 to 2016, there were significant reductions in child labor rates worldwide, with 134 million fewer children working. However, in developing countries, one in four children aged 5 to 17 still engage in hazardous or risky activities that affect their development and do not comply with the international minimum-working-age standards (UNICEF 2019).¹ International initiatives such as employment bans aim to eradicate child labor by implementing a minimum working age and prohibiting the hiring of underage individuals in specific sectors (ILO 2017).

Despite the ratification of the ILO Convention No. 138 by 131 developing countries, little is known about the effectiveness of these bans. Weak enforcement of the law, lack of punishment for non-compliance, and imperfect monitoring could limit their effectiveness. The few studies analyzing the impact of bans find contradicting results (see, e.g., Piza and Souza 2017; Bharadwaj, Lakdawala, and Li 2020; Bargain and Boutin 2021; Lakdawala, Martınez, and Vera-Cossio 2022). This paper evaluates the impact of a complex child labor ban introduced in Mexico on school enrollment and several child labor indicators, offering new evidence and possible explanations for previous diverging findings.

Mexico’s unique setting provides an opportunity to analyze the impact of child labor bans. In 2014, a constitutional amendment increased the minimum working age from 14 to 15 without further regulation. A year later, in 2015, Mexico introduced an ambitious reform to the National Labor Law “Ley Nacional de Trabajo,” one of Latin America’s most extensive initiatives to eradicate child labor. The reform did not only shift the working age from 14 to 15 years but also (a) imposed restrictions on hiring underage individuals,² i.e., under 18 who had not completed basic education (primary and lower secondary), (b) regulated the hiring of individuals between 15 and 18, concerning the type of activities, sector, hours worked, and working schedule, (c) increased penalties for employers violating the regulations, and (d) encouraged agriculture to be child-labor-free. It is important to note that the reform excluded regulating or imposing penalties on subsistence agricultural work. Hence, the goal of this study is to evaluate the impact of these changes: the simple shift in 2014 in the minimum working age and the shift in 2015 coupled with additional employment restrictions and penalties.

The theoretical literature suggests that child labor bans have an ambiguous impact on household welfare. They could improve welfare by encouraging human capital accumulation, or in highly unequal economies, they might affect income distribution and contribute to the persistence of child labor (Baland and Robinson 2000). In very poor regions, such bans may not be effective if households depend on the child’s income or if children need to work to avoid hunger (Basu 1999; Doepke and Zilibotti 2009).³ Indeed, several studies show that poverty is the main reason for parents to rely on child labor, leading them to prioritize current consumption and trade off between child labor and schooling, i.e., future earnings (Basu and Van 1998; Baland and Robinson 2000; Ranjan 2001; Cigno, Rosati, and Guarcello 2002; Jafarey and Lahiri 2002; Horowitz and Wang 2004; Edmonds 2007).

The empirical evidence on child labor bans in developing countries shows minimal impact due to low enforcement or detection methods (Edmonds and Shrestha 2012).⁴ For example, Piza and Souza (2017) find in Brazil that a shift in the minimum working age from 14 to 16 decreases the labor-force participation for 14-year-old boys in the short-run but has no impact on earnings or work in the long-run. In contrast, for the same ban, Bargain and Boutin (2021) find no overall significant impacts in the short run,⁵ but suggestive evidence that child labor decreases in areas where labor inspections were high.

This finding is reinforced by Edmonds and Shrestha (2012), who find no impact of the minimum working age on child time allocation in 59 low-income countries. In contrast, Bharadwaj, Lakdawala, and Li (2020) study a law against child labor in India and find that the ban led to an overall increase in child labor due to a decrease in child wages relative to adult wages. The ban also shifted child labor from banned sectors to other sectors and shifted work from younger to older siblings.⁶ Finally, Lakdawala, Martınez, and Vera-Cossio (2022) analyze changes in the Bolivian law that decrease the legal working age from 14 to 10 and add more benefits and child protection laws for those children. The authors show that child labor for children under 14 decreases in areas where inspection is high.⁷

We contribute to this literature in three different ways. First, our database identifies a wide range of child labor indicators, going beyond previous studies. We focus not only on the probability to work, (in-)formal work, (un-)paid work, wages, sectors, and school enrollment, but also on weekly hours worked, part-time and full-time work, access to a contract, employment benefits, and older siblings. This larger range of indicators allows us to draw conclusions about the type of work and sectors most impacted by the child labor ban and whether the child labor ban shifted the work to older siblings or parents.

Second, this study evaluates the stringency of child labor ban enforcement rather than a simple shift in the minimum working age per se. We compare the impact of a constitutional amendment in 2014, which raised the working age from 14 to 15 without imposing concrete penalties or further regulation on employing minors, with the more complex package introduced by the labor law reform in 2015. This includes examining penalties, regulation of underage work, and basic education requirements to access the labor market to determine the effectiveness of child labor bans.⁸

Third, we exploit survey data collected quarterly for several years before and after the ban to assign individuals to treatment and control groups based on their exact date of birth. Using cross-sectional variation, we track short-run and long-run impacts by following individuals born in the same cohort. The data also provide a limited panel dimension as individuals are followed for five quarters before dropping from the survey.

We further exploit the limited panel dimension to control for unobserved heterogeneity and cohort differences that may vary with age. Specifically, we analyze how the ban affects children with varying pre-reform labor status in the short term and provide descriptive evidence on individuals who comply or do not comply with the ban based on their pre-reform employment status. This is an essential addition to the literature, as no previous study on child labor bans has considered heterogeneity in treatment effects before the reform or provided results beyond an intention-to-treat approach.

Our study uses the minimum-working-age shift as a natural experiment, to analyze data from the Mexican Labor Force Survey (ENOE) for the years 2013 to 2017 (short run) and 2012 to 2019 (long run) on a quarterly basis. Our difference-in-differences (DiD) approach assigns individuals into treatment and control groups based on their date of birth. To identify the effect, we focus on the cohort directly affected by the ban and conduct additional analysis with other cohorts to test the sensitivity of our results. The studies focusing on the Brazilian reform use an RDD approach (regression discontinuity design) (see, e.g., Bargain and Boutin 2021; Piza et al. 2024).⁹ In our context, the ban entirely depends on age at the time the ban is implemented. Individuals born closer to the cutoff would only need to wait some weeks to qualify to work, which could only slightly delay their entrance to the labor market (making it challenging to implement an RDD analysis). In contrast, individuals born further away from the cutoff would have to wait longer to qualify for work. Our within-birth-cohort approach assigns individuals born in the second half of 2000 to the treatment group, as they are 14 years old when the law is enacted and, therefore, banned from the labor force. Individuals born in the first half of 2000 are assigned to the control group, as they are 15 years old when the law is enacted. We further narrow the time frame when exploiting the limited panel dimension by restricting the sample to individuals observed at least one quarter before and one quarter after the change in the 2015 labor law. For the long run, we extend our period to observe treatment and control groups shortly after reaching legal adulthood (at age 18).¹⁰

The empirical approach faces two main challenges. First, individuals born in the same year but at different times may not represent an ideal control group if the birth timing is correlated with unobserved factors that determine schooling and employment decisions, such as age at school start (Fredriksson and Öckert 2014). To address this, we compare individuals born in the same month of the year across different cohorts.

Second, our empirical strategy examines individuals born in the same cohort several quarters (years) after the change in the labor law is implemented. The treatment and control groups reflect the impact of being banned from the labor force for a few days up to a maximum of six months. Some children banned only, e.g., one month, may not be affected as strongly as children who must wait six months to qualify to work. Therefore, we present additional sensitivity analysis using a continuous definition of the treatment based on the number of months a child is banned from the labor force vs. children who are not banned. We estimate both short- and long-run impacts of the change in the labor law using cross-sectional variation. For the short run, we observe the affected cohort two years pre- and post-reform, as well as restrict the sample to children who are just above and below the age of 15 (at the time of the survey) before and after the change in the labor law to address the concerns about children qualifying to work once they turn 15.

Our findings show that increasing the minimum working age alone does not significantly reduce child labor. However, when combined with additional regulation and concrete penalties, it can significantly decrease child labor. The 2014 constitutional amendment had no significant impact on child labor, but a small positive impact on schooling. In contrast, for 14-year-old children, the 2015 labor law reform increased school enrollment by about 2.2 percentage points and decreased the probability of working by about 1.2 percentage points relative to a 15-year-old, representing a 16 percent decrease in the child labor rate for the most conservative estimates, mainly driven by child labor reductions in urban regions and households with low income levels.¹¹ The ban resulted in a decrease in paid activities, particularly in manufacturing and services. The effect of the ban did not transfer to older siblings or parents. Finally, this effect persists even after the affected cohort reaches legal adulthood, as those banned from the labor force are less likely to be employed full time or to be employed and out of school.

These findings show that three main factors influenced the effectiveness of the 2015 labor law reform in reducing child labor: first, increasing penalties for law violations (DOF 2015); second, media coverage emphasizing different aspects of the reforms, such as emphasizing the importance of schooling for the constitutional amendment (Senado de la República 2014), and then the role of penalties for violating the law in 2015 (Martínez 2015). Finally, the General Directorate of the Federal Labor Inspectorate (STPS) increased inspections and awareness campaigns mainly in industries and incentivized agricultural work centers to obtain “child-labor-free” product certificates (STPS 2015, 2017). The number of certified units primarily increased after the shift to the labor law in 2015.¹² While it is true that we cannot distinguish the impact of these measures, our objective is to show that such additional measures highlight the importance of implementing penalties and effective communication strategies to combat child labor effectively.

Therefore, our results suggest that an age ban may be more effective when combined with regulating underage work, requirements to complete basic education, and stricter penalties (consistent with Bargain and Boutin (2021)). In contrast to the framework analyzed for India (Bharadwaj, Lakdawala, and Li 2020), the regulation in Mexico did not simply shift the demand from 14-year-olds to slightly older individuals or other sectors. It made it more expensive for potential employers to hire minors, limiting substitution between 14-year-olds and those aged 15–17 due to restrictions on employment for all minors in various sectors, regulations on working hours and benefits, and the prohibition on hiring minors who have not completed their basic education.

2 Background

2.1 Child Labor Regulation Pre-2015 and Statistics

In 1917, Article 123 of the Mexican Constitution set the minimum age for admission to work at 12 years of age. In 1962, a constitutional amendment raised the minimum working age to 14 and established a six-hour workday for individuals aged 14 to 16, prohibiting night shifts and overtime. This regulation remained unchanged for several years until the signing of the “Convención de los Derechos de Los Niños” in 1989, so that public policies recognize children as subjects of rights and legal protection according to their development and age. In 2000, Mexico ratified the ILO Convention 182 concerning the elimination of the worse forms of child labor (ILO 2020).

Since that date, the Mexican Ministry of Labor and Social Welfare has increased its efforts to prevent and eradicate all forms of child labor. From 2007 to 2012, they implemented an inter-institutional strategy to increase the commitment from different sectors to reduce child labor among minors under 14, protect adolescent workers (above the legal working age), and ensure compliance with national and international legal frameworks for minors. The main objectives in this strategy include generating periodic statistical information on child labor indicators, preventing and eradicating child labor in the agricultural sector, promoting labor rights, and strengthening the legal framework.¹³

Before the 2014 constitutional amendment, indirect efforts to eradicate child labor focused on increasing school enrollment. Public policy targeting child labor indirectly includes, for example, PROGRESA, which began in 1997. This program provides families with additional income, conditional on children being enrolled in school, attending school regularly, and receiving regular health check-ups. PROGRESA led to a substantial increase in school enrollment rates and a modest decrease in child labor (Skoufias et al. 2001). Other programs such as school feeding programs, like school breakfast programs, and initiatives targeted at improving education quality like extending the school day through full-time schools, have also been applied to keep children enrolled in schools.

In Mexico, initiatives targeting child labor became more important due to increased primary- and secondary-school enrollment rates. From 1990 to 2015, school enrollment increased for children aged 6 to 11 from 89 percent to 98 percent, for children aged 12 to 14 from 79 percent to 93 percent, and for individuals aged 15 to 17 from 47 percent to 73 percent (INEE 2018). Upper secondary education became compulsory in 2012, but the regulation is based on school level rather than age (OECD 2018),¹⁴ with no changes to education or minimum schooling requirements,¹⁵ hence limiting the efforts to decrease child labor by increasing schooling.¹⁶

2.2 Constitutional Amendment and Labor Law Reform

Before 2014, the legal framework prohibited children under 14 from working, except for family members. Individuals under 16 were not allowed to work at night or in dangerous conditions, and could only work a maximum of 6 hours per day with no overtime. They were also entitled to a minimum of 16 days of holidays. Employers who violated these rules faced penalties ranging from 3 to 155 times the minimum wage. Prior to 2015, Mexico was one of the last countries in Latin America to ratify the ILO Convention No. 138, which creates national policies to eradicate child labor and sets a “minimum age for admission to employment” into the labor force at 15, the age at which a child leaves compulsory schooling.¹⁷

To ratify the ILO convention, Mexico made two changes: First, on June 17, 2014, the minimum working age was raised from 14 to 15, with no additional regulations introduced (DOF 2014). Second, on June 12, 2015, the Federal Labor Law (“Ley Federal del Trabajo”) was reformed to enforce the new minimum working age (DOF 2015) and imposed stricter penalties for employers hiring individuals under 15. Violations can result in immediate termination of the underage individuals’ work, and a prison term of 1 to 4 years, and/or a fine of 250 to 5,000 times the minimum wage for employers (DOF 2015). The same penalty applies to parents or guardians who allow children to work in hazardous conditions. In addition, the reform in 2015 introduced rules for hiring individuals aged 15 to 17 and set minimum education requirements for minors to join the labor force.¹⁸

After the 2015 labor law reform, the STPS increased child labor inspections in industries, conducting 245,019 inspections from June 1, 2015, to June 20, 2017, and finding children under 15 working in 7,748 of the cases (ILO 2019).¹⁹ Efforts to increase inspections in Mexico have been limited, with the STPS more likely to carry out inspections after a formal complaint. There is no system to track child labor violations, and state-level inspection efforts are not well documented (see, e.g., U.S. Department of Labor 2020).²⁰ Yet the threat of penalties could decrease child labor (see, e.g., Falkenberg and Herremans 1995; Baucus and Beck-Dudley 2005; Waheeduzzaman and Myers 2010; Kaptein 2015). Moreover, the STPS has increased awareness through social media, radio, and TV (STPS 2017). Agricultural work centers have been incentivized to obtain “child-labor-free” certificates, with a significant increase in certified centers from 2010 to 2015 (STPS 2015).

3 Identification Strategy

To analyze the effect of the reform to the labor law introduced in June 2015, we estimate a DiD model exploiting the date of birth as a natural cutoff to define treatment and control groups. In this setup, we observe individuals born in the same cohort and assign them to treatment and control groups according to their month of birth. We focus on the cohort of children who were born in the year 2000 and define the treatment group as children born between June 12 and December 31: they were 14 by the time the reform was implemented. The control group are children born between January 1 and June 11: they were 15 by the time the reform was introduced and thus excluded from the ban.

To analyze the short-run effect of the labor law reform, we focus on the years 2013 to 2017, exploiting cross-sectional variation. This date restriction implies that all individuals in our sample are under 18 and, thus, not legal adults. We focus on this period to have a consistent pre- and post-treatment time frame and control for potential seasonality effects. As a robustness test, we estimate the immediate effect of the reform by focusing on the months before and after the reform for the year 2015. For the long-run effect, we extend the analysis from 2012 to 2019, i.e., when treatment and control groups reach legal adulthood. We estimate the following model for the within-cohort approach:

where Y_imt denotes either child labor or school enrollment for child i, born in month m, at survey time t. For the child labor indicators, we explore (a) the total number of hours worked per week, (b) a binary variable indicating whether the child works (extensive margin), and (c) the number of hours worked conditional on working (intensive margin). We further distinguish between formal and informal work, paid and unpaid work, and type of employment sector. Moreover, conditional on being employed, we analyze the effect on full-time employment, wages, contracts, and benefits received.

Here, |$\mathrm{Born12/06\textnormal {--}31/12_{2000}}$| is a dummy variable that takes the value 1 for children in the treatment group and 0 for the control group; Postban_t is a dummy variable that takes the value 1 after June 2015, when the ban was introduced; and β is the coefficient of interest which captures the differential change in schooling and child labor after the law enactment for individuals below the legal working age compared to those just above it.

The variable X_i is a vector of child characteristics that are likely to affect schooling and child labor, such as household size, gender, and birth order, to control for a higher probability of working for older siblings. Next, P_i is a categorical variable controlling for parental education level, which captures the preference to send children to school and/or work and is a proxy for household income. Furthermore, because work inspections are more likely to occur in areas with a higher level of urbanization, e.g., where formal businesses are registered, we include dummies to control for locality size. Localities are smaller geographical units than municipalities and capture the level of urbanization (high, middle, low, or rural) in the locality the child resides. Unfortunately, sectors like agriculture are only inspected if there is a formal complaint, leaving children vulnerable to child labor (ILAB 2021).

We include birth-month fixed effects δ_m, to consider confounding seasonal factors of being born at different times of the year, and age differences in our within-cohort approach. We also include state fixed effects γ_s to account for state-specific shocks and to capture the regional clustering of industries or sectors more prone to hire individuals under 18. The variable α_t represents quarter-by-year fixed effects as the database used in this analysis is collected on a quarterly basis. The time-fixed effects would capture, for instance, employment or economic shocks that could influence both schooling and child labor. Next, the variable tλ_s accounts for the state-specific linear time trend that captures diverging pre-existing trends in outcomes at the state level or in the intensity of inspections. Finally, the error term is ϵ_imt. Standard errors are clustered at the birth month by survey-year level. We also show that the results are robust to other clustering levels that follow a more liberal approach, such as the birthday-survey-year level, or a more conservative approach, such as the state-by-month-of-birth or birth-month level.

Using the same approach, we conduct the analysis using the main policy change: the constitutional amendment in 2014. In this case, the affected cohort was born one year earlier, i.e., in 1999. This empirical exercise shows the difference between a policy that shifts the minimum working age without concrete penalties for potential employers and the shift in 2015 when penalties and rules for hiring minors were established.

The main identifying assumption of our DiD design is that in the absence of the child labor ban, both groups would have followed the same trajectory. Thus, the main threat to our identification strategy is that the change in the law could shift the labor demand for 15-year-old individuals to replace the labor of 14-year-old individuals. The additional regulations implemented for individuals aged 15 to 17 were a significant impediment to prevent a shift in child labor from one group to another.²¹ Therefore, to show that there is no increase in child labor for the 15-year-olds, we provide graphical evidence on the parallel trends and estimates on employment rates (see fig. 1 above and table 6 of the robustness section).

The second challenge to our within-cohort approach is that 14- and 15-year-old individuals are not fully comparable, so any significant cohort differences are not likely to be invariant to age. We address this concern in two different ways. First, we include individual fixed effects and then look at the heterogeneity in treatment effects by the pre-reform labor status for individuals just above and below 15 at the time of the survey as follows:

The same as in equation (1) holds true, but here individual fixed effects are included in ρ_i since the same individual is observed over time. The variable Z_it is a vector of control variables for children’s time-varying characteristics, such as age and age squared. This specification allows us to estimate the within-individual impact of the ban and account for unobserved time-invariant characteristics at the individual level. We refrain from using this as the baseline (a) because individuals are only followed for five quarters, leading to sample attrition and a considerable decrease in the number of observations, and (b) to facilitate the comparison between the short-run and long-run results.

Second, following equation (1) we implement an across-cohort comparison and use the cohort born in 1999 as a control group to estimate the effect of the labor law reform. To do this, we create two definitions for the treatment and control groups: (a) the treatment group consists of individuals born in 2000 and the control group of individuals born in 1999; (b) the treatment comprises individuals born in the second half of 2000, compared to the control, which includes individuals born in the second half of 1999. Additionally, we provide several placebo tests focusing on non-affected cohorts to show that our estimates are not driven by age differences. Supplementary online appendix table S1.1 summarizes the relevant dates and definitions for the treatment and control groups for the within-cohort and across-cohort comparisons. Moreover, to better understand the variations among different treatment/control groups we present in supplementary online appendix fig. S2.1 the different half cohorts over time and indicate when the constitutional amendment or the labor law reform took place.

Finally, our baseline specification does not take into account the income at the household level. We refrain from including income as a control variable in the main specification and in the analysis in general due to potential endogeneity concerns and the high number of missing values in the income variable. However, we exploit the socio-economic variables to test heterogeneous effects for different poverty definitions which are less likely to be endogenous, e.g., education of the parents, locality size, and marginalization index.

4 Data and Descriptive Statistics

4.1 Data

We use data from the Mexican National Survey on Occupation and Employment (ENOE). The ENOE is Mexico’s largest continuous (rotating) household survey, collected every year on a quarterly basis. The ENOE is the primary source of information on the labor market, employment, informality, and unemployment. The database includes information on 126,000 households per quarter and is representative at the state level. The data provides information on all household members aged 12 years and older. The survey guidelines establish that one main informant provides the information: the individual is usually the household head or the spouse. However, if household members older than 12 were present during the interview, they each provided their information. Therefore, strategic reporting should be acknowledged. In particular, if parents adjust their responses to the survey after the change in the reforms. We believe, however, that the risk is small. The survey is anonymous; no official authorities are collecting this information, and the information is collected through several questions identifying the activities that children perform.

The ENOE provides rich information on schooling and employment,²² as well as on the demographic characteristics of the child, the parents, and the place of residence. We further complement this database using the marginalization level data obtained from the Consejo Nacional de Población (CONAPO) for the year 2010 at the municipality level. The marginalization index is a multidimensional poverty measure considering education, dwelling characteristics, population geographical distribution, and income level (CONAPO 2019). For the main analysis, we focus on the cohort of children directly affected by the reform, i.e., individuals born in 2000 and who are 14–15 years old in 2015. We focus on the survey years 2013 to 2017, i.e., two years before and after the labor law reform, to investigate the short-run impact of the reform.²³ We then extend the time frame from 2012 to 2019 to investigate whether the effects persist after the individual reaches legal adulthood. Additionally, we use data for the cohorts born in 1997, 1998, and 1999 for the across-cohort comparison and placebo tests.

Table 1 provides descriptive statistics for the treatment and control groups before the labor law reform, with a t-test indicating whether the difference in means between groups is significant. Ninety-five percent of children are enrolled in school, and 7 percent are engaged in child labor, working on average 20 hours per week. Most working children are in the informal sector, with only 45 percent receiving compensation for their work. Most work in the tertiary sector (services), with few having written contracts or benefits. Fifteen percent work full-time and earn on average 8 pesos per hour, which equals the Mexican hourly minimum wage in 2015.²⁴ Children live on average in households with five members, with 80 percent living with both parents, and parental education is mostly at the secondary level.²⁵ Finally, 53 percent live in localities that are highly urbanized areas, i.e., localities with more than 100,000 inhabitants.

Comparing pre-treatment means of control and treatment groups shows slight differences, but these differences are usually negligible. For the outcome variables, children in the treatment group are slightly more likely to be enrolled in school and less likely to work before the reform. This occurs because the control group is slightly older than the treatment group, but our specification considers this by including the month of birth fixed effects. Individuals in the treatment group work about half an hour less than individuals in the control group (conditional on working, the difference is about 1.7 hours). The differences are significant for other demographic characteristics but are small in magnitude.

4.2 Descriptive Analysis

We provide graphical evidence of the evolution of school enrollment and employment rates for the treatment and control groups. Figure 1 shows that schooling and employment followed a similar trend before the labor law reform with a minor-level difference between groups. Focusing on schooling, the figure shows a sharp drop for the control group in school enrollment after the second quarter of 2015. This drop is not surprising because usually lower secondary is completed at age 15.²⁶ We also observe a drop in school enrollment for the treatment group, but not as steep as in the control group. The size of the gap between both groups increases considerably after 2015. By the end of 2017, the school enrollment rate of the treatment group remains higher than that of the control group. Focusing on employment rates, we observe a similar pattern, i.e., a common trend before the labor law reform and a gap that opens up after 2015.²⁷ The long-run empirical analyses further allow us to rule out the existence of diverging pre-trends.²⁸

One concern for the parallel trend assumption is that the employment patterns for 14- and 15-years-old are not linear because they follow different employment trends. To alleviate this concern and show that age differences do not drive the effect, but rather the change in the labor law reform, we change the comparison group and use as a control group the previous cohort, i.e., children born in the second half of the year of the previous cohort. The results align with our analysis and show that our parallel trend captures the impact of the reform. The results follow the pattern observed in fig. 1 and are available upon request.²⁹

5 Results

In this section we discuss the baseline results focusing on the reform to the labor law in 2015. Next, we compare and contrast these results with those focusing on the constitutional amendment in 2014 and a placebo reform. We also look at long-term results and provide the results of the heterogeneity and robustness analysis.

5.1 Baseline Results

We start by estimating our baseline specification, focusing separately on the constitutional amendment in 2014 and the labor law reform in 2015. This empirical exercise is of particular interest because it allows us to examine possible anticipation effects and differences in the impact of the two changes to the legal framework. To show further that underlying trends do not drive our estimated coefficients, we also provide the results of a placebo reform introduced in 2013. For each of these policy changes, we estimate the results using a within-cohort approach, where the affected cohorts are determined by the year when the (placebo) policy is changed, i.e., 1998 cohort for the placebo ban, 1999 cohort for the constitutional amendment, and 2000 cohort for the labor law reform.

We estimate the effect of these changes on the probability of being enrolled in school (panel A) and on the probability of being employed (panel B) and report the results in table 2 following our specification in equation (1). The results of the placebo reform reported in column I are not statistically significant for schooling or employment, reducing the concern that underlying group-specific trends drive our findings. Turning to the results of the constitutional amendment in 2014, reported in column II, we observe a statistically significant increase in the probability of being enrolled in school; however, this coefficient represents a slight increase in schooling compared to the pre-reform mean. We further observe no impact on the probability of being employed. The estimated coefficient is close to zero and not statistically significant. The results of the reform in 2014 are consistent with previous studies suggesting that simple shifts in the minimum working age per se are not necessarily successful (see, e.g., Edmonds and Shrestha 2012; Bharadwaj, Lakdawala, and Li 2020; Bargain and Boutin 2021) and could even lead to an overall increase in child labor rates (Bharadwaj et al. 2020). We provide the table with all controls in the supplementary online appendix (see table S1.3.)

In contrast, the estimated coefficients for the labor law reform in 2015 in column III are larger in magnitude and are both statistically significant.³⁰ The estimated coefficients show that the change in the labor law led to an increase in school enrollment by 2.2 percentage points for children in the treatment group relative to children in the control group (panel A, column III).³¹ The results further indicate that the labor law reform (panel B, column III) decreased the probability of being employed by 1.2 percentage points.³² Relative to the pre-reform mean, this translates to an increase in school enrollment by 2 percent and a decrease in child labor rates by 16 percent. The results, however, are in line with studies focusing on the stringency of the laws, such as the heterogeneous impact that Bargain and Boutin (2021) find in areas with low vs. high inspection intensity.³³

While we cannot test directly why the constitutional amendment only operates through schooling rates, newspaper articles can provide some evidence on these results. The public coverage in newspaper and official government channels of the constitutional amendment in 2014 justified the increase in working age as a mechanism to decrease schooling dropout rates (see, e.g., DOF 2014; Senado de la República 2014). In contrast, the newspaper coverage in 2015 of the reform to the labor law, highlighted specifically the restrictions and penalties imposed for potential violations to the law (see, e.g., Martínez 2015). These findings suggest that a mere shift in the minimum working age without establishing (a) concrete penalties for violations to the law and (b) the corresponding legal framework and its enforcement, so that child labor is not simply shifted from one group to another, is not an effective tool to decrease child labor rates. We further provide additional analysis comparing both reforms in the heterogeneous analysis.³⁴

From this point onwards, we focus on the labor law reform 2015 as the main policy of interest due to the strong impacts on child labor rates. Supplementary online appendix table S1.6 further shows the results focusing on total weekly hours worked and hours worked conditional on employment. We observe a decrease in the number of weekly hours worked by about 0.75 hours (45 minutes). The estimated coefficient for conditional hours worked is negative but not statistically significant. The latter suggests that the reduction in hours worked is mainly driven by the extensive margin. Supplementary online appendix table S1.7 further shows that the results are robust to alternative ways of clustering the standard errors.

We further analyze the results focusing on a categorical definition of the treatment, specifically for the labor law reform in 2015.³⁵ The treatment is based on the number of months the child has to wait to qualify to work. We observe consistent results as in the baseline, with stronger impacts for children further away from the cutoff. Children born in June–July are likely to be less affected than those born in November–December. Results are presented in supplementary online appendix table S2.2.

Looking at differential impacts by gender in table 3 (panel A, row I) reveals that after the labor law reform, girls increase their school enrollment by 3.6 percentage points. For boys, the effect is smaller at 0.9 percentage points. For the child labor results, we find larger impacts for girls. Unlike Piza et al. (2024), our results indicate that girls decrease their labor-force participation to a larger extent than boys because girls are more likely to work in the secondary and tertiary sectors.³⁶ Panel A (column II) shows that although boys tend to work more hours, girls are the ones who respond more strongly to the labor law. Girls decrease total hours worked by almost 1.9 hours. The extensive margin and intensive margin (panel A, columns III and IV) show a similar pattern.

Yet when looking at the effect of employment on boys, panel A (column III) shows that the labor law increases the probability of working boys (extensive margin) by 1.1 percentage points, indicating that for a group of boys the reform seems to be ineffective and suggests intra-household allocation of child work (Emerson and Souza 2002; Basu 2006). However, the general effects in the different specifications suggest a general decrease in child labor rates for all the groups that were affected by the reform. The results may be surprising, as girls respond more to the labor law than boys. Additional descriptive statistics in table S1.8 by gender show that, conditional on working, on average, girls work fewer hours per week than boys, especially in the tertiary sector (74 percent in contrast to 43 percent of boys), followed by the secondary sector (16 percent in contrast to 18 percent for boys), and the primary sector (10 percent in contrast to 39 percent for boys).³⁷

5.2 Individual Fixed Effects Results

Next we estimate the impact of the labor law reform exploiting within-individual variation. We restrict the sample to individuals observed at least once before and after the change in the labor law. As individuals are only observed for a maximum of five quarters, this limits the time frame to shortly before and after the reform. The main advantage of this strategy is that it identifies the heterogeneity in treatment effect of children with different work status pre-reform. The pre-reform descriptive statistics for this group are presented in supplementary online appendix table S1.9. In addition, we are able to control for all unobserved heterogeneity at the individual level.

The results presented in table 3 (panel B) show similar findings to the baseline results. Panel B (row I) shows the results for the total sample of individuals. We find an increase in the probability of being enrolled in school and a decrease in the probability of being employed.³⁸ Next, rows II and III show the results for children working and not working before the ban, respectively. The results are consistent with panel B (row I), but the coefficients are much more significant for children working before the change in the labor law was introduced. Taken together, the results suggest that the labor law reform is effective in decreasing child labor in two different ways: it decreased the proportion of working children and simultaneously decreased the proportion of children who would have otherwise (in the absence of the reform) entered employment.

To further test whether accounting for the fixed effects (F.E.) changes the results of the baseline specification, we add supplementary online appendix table S1.11 to show the results of the F.E. model—without accounting for F.E. We observe that the specification without fixed effects for the same subsample slightly overestimates the estimated effects, with much larger estimates for the schooling coefficient and slightly larger impacts for the child labor outcomes. The direction of effects and statistical significance remain unchanged. Interestingly, the results using individual fixed effects and our baseline results are quite similar, suggesting that the control variables included in the baseline specification are capturing several features captured also by the individual fixed effects model.

Importantly, the limited panel dimension of the data allows us to descriptively investigate differences between children who complied vs. those who did not comply with the labor law in supplementary online appendix table S1.12. Compliers are more likely to be in school, work fewer hours, and less likely to have paid employment than non-compliers. They tend to work in the services sector rather than agriculture. This is a first indication that the schooling requirements of the reform actually increased the likelihood of secondary completion. Compliers come from households with fewer members, have slightly more educated parents, and reside in more urbanized areas.

Finally, in supplementary online appendix fig. S1.2, we show descriptive statistics for household income and secondary completion rates. We focus on three groups of individuals in the treatment group: (a) individuals who were not employed pre-reform, (b) individuals who were employed pre-reform and complied with the change in the labor law reform, and (c) individuals who were employed pre-reform and did not comply with the regulation in 2015.

The figure shows that the share of individuals who complete secondary level steadily increases for the first two groups. About 40 percent of individuals who were not employed pre-reform or who complied with the reform report having completed secondary school at age 16. The share of secondary school completion is much lower for individuals who did not comply with the change. While this could be fully attributed to income differences, the second graph of fig. S1.2 shows household income per capita for these three groups. Household income per capita for children who work pre-reform is very similar. After the change in the labor law, income per capita increases slightly for the group of non-compliers and decreases for the group of compliers. The graph shows that removing a child from employment could have an impact on household income in the short run. This decrease, however, may be compensated in the future due to higher completion schooling completion rates for the group of compliers.

5.3 Long-Run Results

Next we estimate whether the labor law reform in 2015 had persistent effects over time. We extend the time frame for the analysis from 2012 to 2019 and follow the cohort born in 2000 until they reach adulthood. The empirical strategy follows the same logic as in equation (1), but we estimate the effect by survey-year to observe (a) differences between treatment and control groups in the pre-treatment period, (b) differences in the period after the reform, and (c) whether these differences are persistent over time.

For this analysis, we focus on the same outcome variables: school enrollment and the probability of being employed.³⁹ However, as working may not be a disadvantage as the cohort gets older and is permitted to work after individuals turn 15, therefore we investigate the impact on other employment variables that may hinder education, i.e., the percentage of children being employed full time or the percentage of children being employed conditional on not being in education.

Figure 2 reports point estimates and confidence intervals at the 95 percent level by survey year. The reference year is 2012. All graphs show no significant differences between treatment and control groups in the pre-treatment period. For the post-treatment we observe a slight decrease in school enrollment when looking at the survey years 2016 and 2017; however, the coefficient is still positive, indicating that the treatment on average has higher school enrollment rates compared to the control group. In addition, a t-test for the two coefficients shows that the difference between the two years is not statistically significant. This is in line with previous studies (see, e.g., Parker, Behram, and Todd 2011; Parker and Vogl 2018; Millán et al. 2019) which show that early school interventions can have positive effects on the outcomes of the children, such as labor-market productivity, human capital accumulation, and educational attainment.

Moreover, when looking at employment, the results show that the effects are more observed when the treated and control groups reach adulthood. This is mainly driven by the fact that the control group turns 18 and is allowed to work. Therefore, to address those concerns of reaching the legal working age, we further run the lower panels of fig. 2 to focus on the outcomes “full-time employment” and “employment: not in education,” which indeed go in line with our baseline specification and yield a negative and statistically significant effect. Therefore, we can conclude from this figure that for the post-treatment period, we observe a significant increase in school enrollment and a decrease in employment, mainly driven by a decrease in the probability of working full time and/or in the probability of working and being out of school (lower panel).⁴⁰

Similar to the findings for Brazil (Piza et al. 2024), these effects seem to last until at least the age of 18, once the individual reaches adulthood. After 2018, individuals in the treatment group reach adulthood and all previous restrictions to enter the labor force do not apply anymore. In this year, there is a spike in school enrollment and employment for the treatment group, which is most likely driven by the slight age difference between groups. The control group reaches adulthood sooner than the treatment group, which leads to a decrease in their school enrollment and an increase in their labor-force participation relative to the treatment group. In 2019, when both groups have reached adulthood, this spike disappears; however, we continue to observe significant differences for the treatment group, but the differences are smaller.

We further conduct the same analysis in supplementary online appendix fig. S1.3 for our two-cohort approach, that is redefining the control group to being born in the second half of the year, i.e., being born between June and December 1999. The results still hold and support our within-cohort comparisons, that is, observing an increase in school enrollment and decrease in employment. The results in this section are further supported by fig. S1.2, where we observe a strong increase in secondary completion for the group of compliers and not employed (pre-reform).

Finally, we estimate the results of a placebo reform in 2013, for the unaffected cohort born in 1998. The results show no statistically significant differences in school enrollment or employment between treatment and control groups for the pre- and post-treatment periods, nor for the probability of working full time or working and being out of school. These results support the findings in fig. 2 that the effect of the change in the labor law is a causal estimate and not mere correlations. Results are available upon request.

5.4 Heterogeneous Effects

5.4.1 Stringency of the Reforms

To further test the effect of penalties we compare the 2014 constitutional amendment (just reform) vs. the 2015 labor law (reform + penalties/regulations) in one model. For the 2014 amendment, cohorts born in 2000 and the second half of 1999 are still young and thus not eligible to work. Therefore, the treatment and control groups are defined as follows: Treatment: the cohort born in 2000 in the first and second halves of the year and the cohort born in the second half of 1999; they are 14 years old in 2014. Control group: the cohort born in 1999 in the first half of the year; they are 15 years old in 2014.

In 2015, the younger half-cohort born in the second half of 2000 are still banned from work, whereas the older half-cohort born in the first half of 2000 have turned 15 in the third and fourth quarters of 2015 and are now allowed to work in 2015. Therefore treatment and control are defined as follows: Treatment group: the cohort born in the second half of 2000; this group is 14 years old in 2015. Control group: the cohort born in 1999 and the cohort born in 2000 in the first half of the year; they are 15 years old in 2015.

Accordingly, we run the four half-cohorts mentioned above in the same model to evaluate the effect of the constitutional amendment vs. the effect of the labor law in a model where we have a relative change based on a scenario where both half-cohorts (second half of 1999 and second half of 2000) were both banned in 2014 and thus can capture the pure effect of the “penalties/regulations” in 2015. The results are presented in supplementary online appendix table S1.13. Looking at the effect of the constitutional amendment in 2014 and 2015 shows that children in the treatment group are more likely to attend school compared to the control group (panel A, column I). This finding suggests that the constitutional amendment positively affected school enrollment for both banned cohorts of 1999 and 2000. However, looking at the effects of the labor law (panel A, column II) reveals that schooling for the treatment in 2014 becomes negative because these cohorts got older and are now allowed to work, whereas the treated cohort 2000 (second half of 2000) are still banned in 2015, thus leading to an increase in school enrollment. As a result, the schooling coefficients indicate that the constitutional amendment and the labor law reform positively affected the treated cohorts. Only when the cohorts get older does the effect start to become negative.

Looking at panel B, table S1.13 shows the employment rate for the four half-cohorts in 2014 and 2015. In panel B (column I), similar to the baseline specification, the results show no effects of the constitutional amendment on employment for both treated cohorts of 2000 and 1999; however, panel B (column II) reveals that the change in the labor law in 2015 increased the employment rate for the treated cohorts in 1999, because those cohorts become older and are allowed to work, whereas for the treated cohort of 2000, the effect is negative on employment, ensuring again that enforcement of the law is only visible when the labor law reform is coupled with penalties for employers that violate the regulations.

5.4.2 Type of Employment and Socio-economic Status

To further analyze the main drivers of the reduction in child labor, we assess the impact of the type of employment and the measures for socio-economic status indicators within the framework of our baseline specification for the short-run effects.

We start by examining the impact of the labor law reform on different types of employment: formal vs. informal work, paid vs. unpaid work, and the sector of employment. The results in supplementary online appendix table S2.3 show a decrease in the probability of being employed in both formal and informal sectors (columns I and II), with a stronger negative impact on paid activities (column III). The reform had a significant impact on employment in the manufacturing (secondary) and services (tertiary) sectors, while agricultural work (primary) remained unchanged (columns V–VII).⁴¹ This is consistent with the idea that subsistence work will remain unaltered because the family depends on it to cover their basic needs (see, e.g., Basu, Das, and Dutta 2010). These results also explain the larger decrease in employment for girls, who tend to work in the secondary and tertiary sectors, while boys concentrate in the primary sector. It is true that unpaid work is less subject to controls and penalties; however, when looking at the mean of formal work it shows that in absolute terms the decrease for formal work (100 percent) is way larger than that for informal work (8 percent), indicating that the reform affected visible/detectable work more.

Most penalties, e.g., through inspections, are more common in urbanized areas for services and manufacturing industries, making it costlier for some employers to hire underage individuals. Although these restrictions could be overseen by employers in the informal sector, if child labor is visible⁴² they could also be subject to penalties. For children who continue to work, the reform decreases the probability of full-time work and access to benefits, but has no significant impact on wages.⁴³ Results are presented in supplementary online appendix table S2.4, showing that enforcement of labor regulation can push workers to informality (Almeida and Carneiro 2012). The results of tables S2.3 and S2.4 should be interpreted with care due to potential selection issues in the sample. However, the results help provide insight into how children adjust to the labor law and the type of work they are doing.⁴⁴

We also explore whether the results are heterogeneous using different socio-economic measures such as the education of the parents, locality size, marginalization index, and the region of residence. The results are reported in fig. 3, showing point estimates and confidence intervals of the effect of the labor law interacted with the respective income (regional) classification and reporting marginal effects.

Panel A shows the results of an interaction between the effect of the labor law and the education indicator for the fathers. This socio-economic variable acts as a proxy for income. The education level indicates whether the father has no education, primary, secondary, high school, vocational training, or a university degree. Panel B presents the locality size, which captures the urbanization level and is also correlated with the region’s poverty level. Panel C shows a categorical indicator that reflects whether the municipality where the child lives has a low, average, or high marginalization index. We interact it with the labor law reform, using data from CONAPO (2019). Finally, to explore the heterogeneity in law enforcement, we focus in panel D on the region where children reside.

Accordingly, fig. 3 shows that the probability of being employed decreases for children who have fathers with no, primary, or secondary education (panel A).⁴⁵ The effect is concentrated for children with fathers who have no education. The results on school enrollment are positive and significant for all education levels of the fathers. In contrast, the decrease in employment mainly happens in areas with a low marginalization level, primarily urban areas (panels B and C). Children living in these areas also drive the increase in the probability of attending school. Finally, the results in panel D show a pattern similar to panels B and C, that is, a decrease in employment mainly concentrated among children living in the center of Mexico. This indicates that law enforcement was mainly present in the regions located in the center. As for school enrollment, we observe a positive effect of the reform for almost all regions.

Taken together, the results in fig. 3 suggest that poor children (having parents with low education levels) but who live in urban areas, mainly in the center of Mexico, are the ones that respond more to the labor law reform. This further indicates that law enforcement was mainly implemented in urban areas, more precisely in the regions of Mexico located in the center. It is important to note that if child labor were only present in rural areas or only in very low-income families, then the results in this section may not represent a large reduction in employment. However, the descriptive statistics in table S1.14 show that 34 percent of children who work aged 14–17 live in urban areas and that 77 percent of children who work live in households that are extremely poor, or poor, and 23 percent of the working children live in households above the poverty line.⁴⁶

5.5 Robustness Checks

We address the main concern that our estimates could be partially driven by the age difference between our treatment and control groups by focusing on across-cohort comparisons instead of within-cohort comparisons.

Therefore, we test the sensitivity of our results in table 4 by implementing across-cohort comparisons for a placebo ban in 2013 (column I), the constitutional amendment in 2014 (column II), and the shift to the labor law in 2015 (column III). We focus on the cohort directly affected and the cohort born one year earlier. For instance, for the labor law reform in 2015, we use information on the cohorts born in 1999 and 2000 (see supplementary online appendix table S1.1 for the full description). The treatment group contains individuals born in the second half of the year (June to December), and the control group consists of those born in the first half (January to June). We interact this variable with a policy variable that takes the value 1 after June 2015. We include the full set of control variables, fixed effects, and further control for cohort fixed effects. The results are similar to the baseline results, with slightly smaller point estimates indicating that children in the treatment are more likely to enroll in school and less likely to work.

Second, in supplementary online appendix table S1.17, we further refine the definition of the treatment and control groups of the across-cohort comparison, by restricting the sample to individuals who are born in the second half of the year, e.g., for the baseline estimates we define the treatment group as individuals born between June and December of 2000 and the control group as individuals born between June and December of 1999. Similarly, for the constitutional amendment and placebo reform, we focus on the 1997–1998 and 1998–1999 cohorts, respectively. The estimates remain robust. We observe an increase in schooling and a decrease in employment when focusing on the 2015 labor law reform.

The previous two approaches, however, do not solve the concern that, at some point, all treated children are legally allowed to work. While the primary purpose of our study is to evaluate the impact of being subject to a ban and how this ban could have long-run effects, to test the robustness of our results, we also estimate the impact of the ban for children close to the age of 15 at the time of the survey. Therefore, to estimate the effect of not being legally allowed to work, we estimate a child fixed effects specification and compare children above and below the age of 15 when the survey was implemented before and after the reform. This implies that we compare children born in different cohorts (1998–2004) right when they turn 15 before and after the labor law reform in 2015. Therefore, in table 5, we redefine treatment to be a dummy variable for being at least 14 years old post-reform and control to be children who are 15 years old post-reform. The results align with the baseline results and show no jumps after a child’s 15th birthday. This means we see a decrease in hours worked driven by the extensive margin.

The final concern is that the labor law might shift child work to less visible forms without reducing it, such as reallocating work within the household from younger siblings to older siblings or parents. We show this empirically by estimating the impact of the reform on individuals who have a younger sibling affected by the reform. The same logic applies as in equation (1); however, we define the treatment as individuals aged 15 to 17 with a younger sibling aged 7 to 14 years old and, thus, banned from the labor force. For the comparison group, we focus on individuals aged 15 to 17 with no younger siblings aged 7 to 14. Table 6 shows no significant effects of the labor law reform on the labor-force participation of individuals with a younger sibling affected by the reform. Moreover, we further run the same analyses to check the effect of the reform, conditional on having at least one treated child in the household, on parents’ labor-force participation, conditional hours worked, domestic work, and time to take care of children, and find no effects, either for mothers or for fathers. Results for parents are available upon request.

6 Conclusion

This paper contributes to the limited research on how child labor bans impact school enrollment and child labor in developing countries, specifically by comparing the stringency of different policies. Our results are unique because we are the first to exploit the panel structure of our data to make some inferences about compliers and non-compliers, look at heterogeneous treatment effects pre-law-change labor status, and provide insights for the long run. We provide evidence of two relevant events that define the legislation in Mexico concerning child labor: a constitutional amendment in 2014 that raises the minimum working age from 14 to 15, without further regulation, and the labor law reform in 2015 that includes (a) concrete penalties for employers, (b) minimum schooling regulations for hiring individuals under 18, and (c) specific regulations for hiring individuals over 15 who have not reached legal adulthood.

Using data from the Mexican Labor Force Survey (ENOE), we implement a DiD approach that exploits the date of birth as a natural cutoff to assign individuals into treatment and control groups. Unlike child labor ban studies in India and Brazil (Bharadwaj, Lakdawala, and Li 2020; Bargain and Boutin 2021), we find that the ban led to a decrease in child labor, but only after the 2015 labor law included stricter regulations. We also consider the impact of media coverage on these reforms’ effectiveness. Evaluating the heterogeneity in exposure to the media and child labor outcomes could be an interesting avenue for future research (see, e.g., Kearney and Levine 2015; Philippe and Ouss 2018 ).

Our short-run results show that the reform increases school enrollment by 2.2 percentage points and decreases the likelihood of working by 1.2 percentage points. These findings are consistent even when individual fixed effects are included. This is a significant impact, equivalent to a 2 percent increase in school enrollment and a 16 percent decrease in child labor. Precisely at the threshold between 14 and 15, a back-of-the-envelope calculation shows that due to the ban in 2015, 25,000 teens stopped working in child labor, and almost 50,000 potential dropouts opted to stay in school rather than enter the labor force. Our findings show that the decreased likelihood of working is mainly due to decreased paid activities in the secondary and tertiary sectors. In contrast to Piza et al. (2024), we observe a stronger impact of the ban on reducing child labor for girls, who are more likely to work in these sectors. We find no effect on children working in the agricultural sector or those living in highly marginalized rural communities, as the regulation does not apply to work for personal consumption. Instead, the effects are concentrated among the poor population in urban regions. We also show that due to the ban, the increase in school enrollment and decrease in employment persist over time. The treatment group is less likely to work full time or be employed and out of school after reaching legal adulthood.

The results in this study are of particular relevance because of the current proposal to lower the minimum working age in agriculture in Mexico from 18 to 16, which is being discussed in the senate (Cantú 2022). Agriculture is considered hazardous due to heavy physical work, use of heavy equipment, and handling of toxic substances. If the shift is approved, policymakers must ensure that young people in rural areas have safe working conditions and opportunities to stay in school.

For policymakers, our study highlights the importance of policies establishing a minimum working age to join the labor force. These policies are a useful instrument not only to decrease child labor but also to increase school enrollment. However, our results also show that the enforcement of the law is essential and that a mere shift in the minimum working age is not effective if these policies are not coupled with concrete penalties for potential employers who hire child labor and specific regulations for hiring underage individuals (e.g., minimum education requirements, reduction in working hours). Finally, the limitations of these policies to decrease child labor related to subsistence work for very poor households in rural areas also need to be acknowledged.

Data availability

The data in this article are in the public domain, available at https://www.inegi.org.mx/programas/enoe/15ymas/#Microdatos. The code is available upon request.

Author Biography

Mireille Kozhaya (corresponding author) is a doctoral researcher at the University of Wuppertal and at the WIB – Wuppertal Research Institute for the Economics of Education, Wuppertal, Germany; her email address is [email protected]. Fernanda Martínez Flores is a researcher at the RWI – Leibniz Institute for Economic Research (Essen); her email address is [email protected]. The authors thank Thomas K. Bauer, Ronald Bachmann, Christian Bredemeier, Julia Bredtmann, Eric Edmonds (the editor), Caio Piza, Kerstin Schneider, Franz Westermaier, David Zuchowski, and three anonymous referees for their constructive comments. Rachel Kuhn provided excellent research assistance. We also thank the participants of the internal research seminars at the University of Wuppertal, and the participants of the Annual Conference of the European Society for Population for their constructive comments. A supplementary online appendix for this article can be found at The World Bank Economic Review website.

Footnotes

References