The Long-Run Effects of Teacher Strikes: Evidence from Argentina

We exploit cross-cohort variation in the prevalence of teacher strikes within and across provinces in Argentina to examine how teacher strikes affect student long-run outcomes. Being exposed to the average incidence of strikes during primary school reduces labor earnings of males and females by 3.2% and 1.9%, respectively. A back-of-the-envelope calculation suggests that this amounts to an aggregate annual earnings loss of $2.34 billion. We also find an increase in unemployment and a decline in the skill levels of the occupations into which students sort. These effects are driven, at least in part, by a reduction in educational attainment.


I. Introduction
Teacher industrial action is a prevalent feature of public education systems across the globe; during the past few years, teacher strikes have been observed in Argentina, Canada, Chile, China, France, Germany, India, Israel, Lebanon, Mexico, Russia, and the United States (e.g., Charleston, Seattle, East Saint Louis, Pasco, Prospect Heights, and Chicago). A shared belief among policy makers across several of these countries is that teacher strikes disrupt learning and negatively impact student educational attainment. In some countries, this sentiment has led to the enactment of legislation that severely restricts teachers' right to strike. 1 However, despite the prevalence of teacher strikes across the globe-and the debates surrounding them-there is a lack of empirical work that credibly examines how they affect student long-run outcomes.
In this paper, we construct a new data set on teacher strikes in Argentina and use this to present the first evidence in the literature on the effect of school disruptions caused by teacher strikes on student long-run outcomes. Between 1983 and 2014, Argentina experienced approximately 1,500 teacher strikes, with substantial variation across time and provinces, making this a particularly interesting case for the study of teacher strikes. We analyze the relationship between exposure to strikes in primary school and relevant education, labor market, and sociodemographic outcomes when the exposed students are between 30 and 40 years old. 2 We also examine whether the effects that we identify carry over to the individuals' children.
To identify the effect of strike-induced school disruptions, we rely on a difference-in-differences method that examines how education and labor market outcomes changed among adults who were exposed to more days of teacher strikes during primary school compared to adults who were exposed to fewer days of strikes. The sources of variation that we exploit come from within-province differences in strike exposure across birth cohorts and within-cohort differences in strike exposure across provinces. On average, provinces lost 372 instructional days due to strikes between 1983 and 2014, ranging from 188 days in La Pampa to 531 days in Rio Negro. The average number of primary school days lost due to teacher strikes was 88 among the individuals in our analysis sample-equivalent to half a year of schooling. 3 1 For example, even though 33 states in the United States have passed duty-tobargain laws that require districts to negotiate with a union, only 13 states allow teachers to go on strike in the event of a bargaining impasse (Colasanti 2008). 2 We focus on this age range because existing literature suggests that labor market outcomes at this age are informative about lifetime outcomes (e.g., Böhlmark and Lindquist 2006;Haider and Solon 2006). 3 It is important to highlight that the pervasive level of teacher strikes during our analysis period is not a deviation from the norm in Argentina and that current students are exposed to similar levels of strikes.
The main assumptions underlying our estimation strategy are that there are no shocks (or other policies) contemporaneous with teacher strikes that differentially affect the various cohorts and that the timing of teacher strikes is uncorrelated with prior trends in outcomes across birth cohorts within each province. We show extensive evidence that our data are consistent with these assumptions. In particular, our results are robust to controlling for local labor market conditions, including province-specific linear time trends, accounting for cross-province mobility, excluding regions with persistently high frequencies of teacher strikes, and controlling for province-specific nonteacher strikes. We also show that the effects that we identify disappear when reassigning treatment to cohorts that have just graduated from-or have not yet started-primary school, indicating that the timing of teacher strikes is uncorrelated with trends in outcomes across birth cohorts within each province over time.
We find robust evidence in support of adverse labor market effects when the students are between 30 and 40 years old: being exposed to the average incidence of teacher strikes during primary school reduces wages for males and females by 3.2% and 1.9%, respectively. We find some suggestive evidence that exposure to strikes in early grades has larger effects than exposure in later grades, though these differences are often not statistically significantly different from zero. The prevalence of teacher strikes in Argentina means that the effect on the economy as a whole is substantial: a back-ofthe-envelope calculation suggests an aggregate annual earnings loss of $2.34 billion. This is equivalent to the cost of raising the average employment income of all primary school teachers in Argentina by 62.4%.
In addition to adverse wage and earnings effects, our results reveal negative effects on several other labor market outcomes. With respect to males, we find evidence of both an increase in the likelihood of being unemployed and occupational downgrading. The effects are very similar for females. However, instead of occupational downgrading, we find an increase in home production (neither working nor studying). Our analysis suggests that these adverse labor market effects are driven, at least in part, by declines in educational attainment: being exposed to the average incidence of strikes leads to a reduction in years of schooling by 2.02% and 1.58% for males and females, respectively. By looking at 12-17-year-olds, we show that negative education effects are visible immediately after children have finished primary school and that they are larger among children from more vulnerable households. Our analysis reveals that strikes affect individuals on other sociodemographic dimensions as well. Specifically, individuals exposed to teacher strikes have less educated partners and lower per capita family income. Finally, we find significant intergenerational effects: children of individuals exposed to strikes during primary school suffer negative education effects as well.
Our paper contributes to the existing literature in several ways. First, no other paper has examined the effects of strike-induced school disruptions on students' long-run labor market outcomes. Given the large literature demonstrating that short-run program effects on student outcomes can be very different from long-run effects (e.g., Chetty et al. 2011;Deming et al. 2013;Lovenheim and Willén 2019), this is of great value to policy makers. Second, the prevalence of teacher strikes that we exploit is much greater than that which has been used in earlier studies. This allows us to obtain more precise estimates and examine a richer set of outcomes. Third, this paper makes use of a new data set that we have created based on information from historic business reports on the Argentine economy. This data set is a great tool for other researchers interested in questions centering on teacher strikes and industrial action.
This paper proceeds as follows: Section II provides an overview of the education system in Argentina and offers theoretical predictions of how teacher strikes may affect student outcomes; Section III discusses preexisting research; Section IV introduces the data; Section V presents our empirical strategy; Section VI discusses our results; and Section VII concludes.

A. The Argentinian Education System
Education in Argentina is the responsibility of the provinces and is divided into four stages: kindergarten, primary education, secondary education, and tertiary education. 4 Primary education begins in the calendar year in which the number of days that the child is 6 years old is maximized and comprises the first 7 years of schooling. During our analysis period, only primary education was mandatory in Argentina (Alzúa, Gasparini, and Haimovich 2015). 5 Since then, compulsory schooling has grown to include secondary education as well, increasing the length of mandatory education from 7 to 12 years. Public education is financed through a revenue-sharing system between the provinces and the federal government and is free at all levels.
The fraction of students who attended private school at the primary level during our analysis period was approximately 0.18, and this fraction remained relatively constant across the years that we examine. Since 2003, however, private enrollment at the primary level has increased substantially. Existing research suggests that this increase is driven by high-and middleincome families, leading to an increase in socioeconomic school segregation between private and public schools (Gasparini et al. 2011b;Jaume 2013). 6 4 Primary education was decentralized in 1978, and secondary education was decentralized in 1992. However, the national government remains highly involved in terms of setting curriculum, regulations, and financing. 5 The youngest cohort in our main analysis sample finished primary school in the year prior to the implementation of the Federal Education Law (1998;approved in 1993), which extended mandatory education to encompass secondary schooling as well. 6 A commonly held belief is that individuals perceive private education as superior since teacher strikes are less pronounced at these institutions, but existing literature

B. Teacher Strikes in Argentina
The presence of unions, collective bargaining, and labor strikes in Argentina can be traced back to the early years of the twentieth century, except for the years during which the country was subject to military dictatorships (CEA 2009). 7 Following the most recent reinstatement of democracy (1983), industrial action has quickly regained its status as a pervasive feature of the Argentinian labor market. Since then, public sector teachers have been the most active protesters in the country, making up 35% of all strikes (Etchemendy 2013). In comparison, private school teachers account for less than 4% of the country's strikes. The occupation with the second-most strikes is public administration, accounting for 25% of the country's strikes (Chiappe 2011;Etchemendy 2013).
Teacher unions are typically organized at the provincial level, and variation in teacher strikes across time and provinces is substantial. On average, provinces have lost 372 instructional days due to teacher strikes between 1983 and 2014 (6.7% of total instructional days), ranging from 188 days in La Pampa to 531 days in Rio Negro, with a standard deviation of 109 days. 8 The pervasive level of strikes during our analysis period is not a deviation from the norm in Argentina, and current students are exposed to similar levels of strikes. Figure 1A shows the variation in the number of days of teacher strikes by province from 1977 to 2014, and figure 1B displays the number of strikes by province during the same period (a strike can last for a single day or several weeks).
No study has examined the effect of teacher strikes on student outcomes in Argentina, but two studies have attempted to disentangle the factors underlying the prevalence of teacher strikes in the country. The results are mixed: Murillo and Ronconi (2004) find that teacher strikes are more common in provinces where union density is high and political relations with the local government are tense, while Narodowski and Moschetti (2015) conclude that strikes display an erratic behavior without any discernible trends or explanations. What these studies have in common is that they both emphasize the lack of a relationship between local labor market conditions and teacher strikes. This is important since our main identification assumption is that there are no shocks contemporaneous with teacher strikes that differentially affect the different cohorts-something we explore at length in Section VI.C. finds no effect of teacher strikes on the likelihood of being enrolled at a public institution (Narodowski and Moschetti 2015). We examine this in detail in Sec. VI.D. 7 During the dictatorships, labor strikes were prohibited and collective bargaining was limited. 8 In theory, days canceled due to adverse circumstances must be rescheduled. However, the prevalence of teacher strikes across time means that this rarely happens. FIG. 1.-Variation in teacher strikes, 1977-2014 Authors' tabulations are based on historic reports on the Argentine economy published by Consejo Técnico de Inversiones (1977-2014. A, Number of days of teacher strikes for each province (including national teacher strikes). B, Number of teacher strikes for each province. The variation to the left of the vertical line is used in our main analysis when we examine long-run outcomes. The variation to the right of the vertical line is used in our supplemental analysis in Section VI.D when we look at short-run outcomes.

C. Theoretical Predictions
This paper exploits variation in teacher strikes within and across provinces over time to identify the reduced-form effect of teacher strikes on student outcomes. As such, this is not a full analysis of the benefits and costs associated with teacher strikes but rather a partial equilibrium analysis that uses strikes to measure the effect of school disruptions on students' outcomes. Specifically, we are not measuring the benefits or costs in a general equilibrium (GE)/dynamic sense. For example, the ability of teachers to strike may give them leverage in negotiations, leading to changes in working conditions that attract a different quality of teachers or affect investments in schooling, and this may impact future student cohorts. 9 In this section, we provide a discussion on a large subset of the potential implications of teacher strikes. This should not be viewed as an exhaustive list but rather as an overview of some of the more common ways in which teacher industrial action can impact students. In addition to serving as an overview of what teacher strikes may do, this section is imperative for understanding which subset of these factors our empirical strategy is able to pick up.
The main way in which strikes can affect student outcomes is by reducing the time that students spend in school. Theoretical as well as empirical research provides clear predictions that reduced instructional time lowers academic achievement (Cahan and Cohen 1989;Neal and Johnson 1996;Lee and Barro 2001;Gormley and Gayer 2005;Cascio and Lewis 2006;Luyten 2006;Marcotte 2007;Pischke 2007;Marcotte and Helmet 2008;Sims 2008;Leuven et al. 2010;Fitzpatrick, Grissmer, and Hastedt 2011;Hansen 2011;Goodman 2014;Rivkin and Schiman 2015). However, these papers examine only the short-run educational effects of school disruptions.
In addition to reducing effective instructional time, teacher strikes may (among other things) affect teacher effort, alter resource levels and allocation, affect academic expectations and graduation requirements, alter the value of a diploma, change the value differential between a public and a private degree, and change the composition of teachers. The direction and magnitude of the effects flowing through these channels will depend on the nature and outcome of the strike. For example, if the unions go on strike to bargain for higher wages and are successful, the strike may improve teacher effort and productivity. However, if the teachers are unsuccessful and the strike is in effect for several months, academic expectations and graduation requirements may be adjusted downward, with the potential implications of a reduction in the value of a diploma. Further, even if the teachers are successful, an increase in teacher pay may be financed through a reallocation of resources from other inputs that enter the education production function, and this can lead to a reduction in education quality.
The above discussion makes clear that the effect of teacher strikes on education production can be both positive and negative, and the resulting predictions of the effects of teacher strikes on student outcomes are therefore ambiguous. With respect to the current study, it is important to note that we use teacher strikes to measure the effect of school disruptions on student long-term outcomes through a partial equilibrium analysis. To the extent that the above factors impact current students, they will contribute to the effects that we estimate. However, some of the factors discussed above may impact only future student cohorts, and our estimation strategy does not allow us to fully identify those effects. 10 In addition to having direct effects on student education outcomes, teacher strikes may impact several noneducational outcomes as well. For example, unless parents can make alternative childcare arrangements (which will depend on whether it was an expected or unexpected strike and on the resources that the parents possess), strikes will increase leisure time and the risk that students engage in bad behavior and criminal activity (e.g., Henry et al. 1999;Anderson 2014). This can directly impact the future education and labor market outcomes of children. Though we cannot directly look at the relationship between strikes and engagement in criminal activity, to the extent that this occurs and affects the long-run outcomes of students, it will be a part of the effects captured by our point estimates.
A final factor that makes it difficult to anticipate the likely effects of strikes on student outcomes concerns treatment heterogeneity. The most likely source of heterogeneity relates to the socioeconomic characteristics of the students' 10 To obtain suggestive evidence on the effect of strikes on future student outcomes, we have reestimated our baseline equation using exposure to strikes prior to start of school as our treatment variable. If teacher strikes affect future student outcomes, we would expect this analysis to return significant results. The results from this exercise are shown in panel H of table 7. All point estimates are small and not statistically significant, suggesting that our data are inconsistent with this idea. Given the large number of students affected by teacher strikes in Argentina, there could also be GE effects at the labor market level (for a discussion on how large educational shocks may generate GE effects on the labor market, see Moretti [2004] and Jaume [2017]). For example, old cohorts might benefit from younger cohorts being exposed to strikes since that lowers the competition that they face on the labor market. However, we provide suggestive evidence that these GE effects are not driving our results through a placebo test. Specifically, we reassign the treatment variable for birth cohort c to birth cohort c-7, such that the measure of exposure to teacher strikes is the number of days (in tens of days) of primary school strikes that took place while the individuals were 13-19 years old (panel E of table 7). If teacher strikes affect past student cohorts (e.g., through reductions in labor market competition), we would expect this analysis to return significant and positive results. This exercise returns small and not statistically significant results, suggesting that this type of GE effect is not driving our results. families: wealthy parents will be able to move their children to private school if they believe strikes to hurt their children. Depending on the prevalence of this behavior, it may lead to a segregated school system with additional adverse effects on the students left behind. Another source of heterogeneity relates to the specific point during primary school at which children are exposed to strikes. Research suggests that young children are more susceptible to policy interventions in general, and children who lose instructional time in first grade may suffer more than children who lose instructional time in the final grade of primary school (Shonkoff and Meisels 2000;Cunha and Heckman 2007;Chetty, Hendren, and Katz 2016). Finally, the effect of several short disruptions may be very different from the effect of one long disruption. We explore all these types of heterogeneity in Section VI.C.

III. Prior Literature on Teacher Strikes
The majority of the existing research on teacher strikes is cross sectional with identification strategies that are vulnerable to omitted variable bias (Caldwell and Maskalski 1981;Caldwell and Jefferys 1983;Zirkel 1992;Thornicroft 1994;Zwerling 2008;Johnson 2009). Specifically, students, teachers, and schools subject to strikes may be different from those that are not subject to strikes on dimensions that we cannot observe. If these differences have independent effects on the outcomes that we look at, this will bias the results. Further, these studies have focused on contemporaneous effects (test scores) of teacher strikes that are of very short duration. These two factors significantly limit our understanding of the consequences associated with school disruptions caused by teacher strikes. This is particularly the case given the large literature suggesting that short-run program effects on student outcomes can be very different from any long-run effects (e.g., Chetty et al. 2011;Deming et al. 2013;Lovenheim and Willén 2019).
Abstracting away from potential identification issues, the results from the above studies are mixed. While some studies find no association between strikes and student outcomes (e.g., Zirkel 1992;Thornicroft 1994;Zwerling 2008), others find marginally statistically significant and negative effects (e.g., Caldwell and Maskalski 1981;Caldwell and Jefferys 1983;Johnson 2009). Taken together, these studies suggest that school disruptions caused by teacher strikes have a minimal impact on student outcomes. 11 To the best of our knowledge, only two studies on teacher strikes and student outcomes have relied on research designs that are not cross sectional: Belot and Webbink (2010) and Baker (2013). Belot and Webbink (2010) exploit a reform in Belgium in 1990 that led to substantial and frequent strikes in the French-speaking community but not in the Flemish-speaking community of the country. By comparing the difference in education outcomes between individuals in school to those not in school in the Frenchspeaking community to that same difference in the Flemish-speaking community, the authors find that strikes cause a reduction in education attainment and an increase in grade repetition. Though interesting, this paper is not able to examine whether the education effects carry over to the labor market, whether there are noneducational effects of teacher strikes, and whether there are intergenerational effects. Further, the point estimates in Belot and Webbink (2010) provide the intent-to-treat effect of exposure to all strikes in 1990 among students in all grade school years. This makes it difficult to extrapolate the marginal effect of teacher strikes on students in specific grade years. Baker (2013) evaluates the effect of teacher strikes on student achievement in Ontario by comparing the change in test score between grades 3 and 6 for cohorts exposed to a strike to the corresponding change for cohorts that were not subject to a strike. The results suggest that strikes that lasted for more than 10 days and took place in grades 5 or 6 have statistically and economically significant negative effects on test score growth, while strikes that occurred in grades 2 or 3 do not. However, data limitations prevent the author from examining long-run education and labor market effects-one of the main contributions of the current analysis.
To summarize, the majority of the existing research on teacher strikes is cross sectional with identification strategies that are vulnerable to omitted variable bias. More current papers rely on identification strategies less susceptible to such issues, but limited variation in teacher strikes coupled with poor outcome data has led these studies to examine only the short-and medium-term educational effects of strikes. To the best of our knowledge, no paper has explored the long-run educational attainment and labor market effects of teacher strikes. Further, no study has examined whether there are intergenerational effects associated with teacher strike exposure.

A. Teacher Strikes
Data on teacher strikes are obtained from historic reports on the Argentine economy published by Consejo Técnico de Inversiones (CTI). These reports provide province-specific information on strikes per month, and we use information from 1977 to 1998 to construct our data set. We assume that children begin school in the calendar year that they turn 6 and graduate from primary school at the age of 12. This means that we have information on exposure to teacher strikes while in primary school for children born between 1971 and 1985. 12 12 The assumption that children attend primary school between the ages of 6 and 12 leads to some measurement error in treatment assignment because children start For our main analysis, we restrict attention to teacher strikes in primary school. Results from specifications that use strike exposure during primary school and potential strike exposure during secondary school are shown in the appendix (available online). 13 Our decision to focus on strikes in primary school is based on data limitations and the fact that there are multiple levels of selection that complicate the analysis of strike effects in secondary school.
First, our data on teacher strikes are not representative of teacher strikes in secondary school. Specifically, the data that we have collected from the historic records of CTI convey information about primary school teacher strikes, and the educational system in Argentina was structured in such a way that secondary school teachers were unlikely to join primary school teachers on their strikes. 14 It is also important to note that secondary education was decentralized at the province level only after 1992 and that they therefore most likely did not participate in any of the province-specific strikes that took place prior to this year. This means that our treatment measure is incredibly noisy and oftentimes wrong with respect to exposure in secondary school.
Second, during our analysis period, only primary education was mandatory (less than 60% attended secondary school). This is problematic not only because it will force us to assign incorrect treatment dosages in secondary school to more than 40% of the population but also because it introduces a substantial selection problem: if school disruptions in primary school affect educational attainment, it may impact who enters secondary education, causing selection bias. 15 primary school in the calendar year in which the number of days that they are 6 years old is maximized. This assumption will thus slightly attenuate our results. Using household survey data on the educational attainment of 6-year-olds between 2003 and 2015, we estimate that more than 70% of individuals in our sample are assigned to the correct cohort. 13 The effect of exposure to strikes in primary school is robust to the inclusion of potential exposure to strikes in secondary school-all point estimates are within the 95% confidence interval of the baseline results. The effect of potential exposure to teacher strikes in secondary school has no effect on student long-run outcomes. As noted in the text, we do not believe that this represents effect heterogeneity but rather treatment heterogeneity caused by measurement error and selection bias (i.e., that children of secondary school age were usually not subject to strikes). Because of this, we believe that the correct level of analysis is exposure in primary school.
14 To obtain suggestive support for this, we have randomly selected some of the strikes reported by CTI and examined what was written about these strikes in the national newspapers at the time of those strikes. In all cases, the national newspapers report that primary school teachers participated in the strikes and that secondary school teachers participated only occasionally. 15 This selection concern is something that we find suggestive evidence of with respect to the likelihood of finishing secondary school (table 2) and enrollment Third, private school enrollment was very high at the secondary level (30%) during our analysis period, and strikes are much less prevalent in the private sector: while public teachers make up about 35% of all strikes in Argentina, private teachers account for less than 4%. This is much less of an issue at the primary level since enrollment in private schools was half that of enrollment in private schools at the secondary level. Table 1 depicts our identifying variation. Looking across the table, there is substantial variation both within provinces over time and across provinces in any given year. Table 1 also shows that the average number of days of teacher strikes that these cohorts were exposed to during primary school is 40 (3.2% of primary school). 16 If one takes national teacher strikes into account, this number increases to 88 (6.98%). 17 As discussed in Section II, strikes were prohibited during the military junta of 1977-83. This explains why the oldest cohorts in our sample are exposed to fewer days of teacher strikes.

B. Long-Run Outcomes
Our main outcome data come from the 2003-15 waves of the Encuesta Permanente de Hogares (EPH), a household survey representative of the urban population of Argentina (91% of the population). We restrict our analysis to individuals between the ages of 30 and 40 because these individuals are typically on a part of their earnings profile where current earnings are reflective of lifetime earnings (e.g., Böhlmark and Lindquist 2006;Haider and Solon 2006). Figure 2 shows the data structure for a sample of birth cohorts. 18 Critical to our identification strategy is our ability to link respondents to their province of birth, because teacher strikes may lead to selective sorting across provinces, especially if exposure to strikes affects school quality. Teacher strikes could also impact post-primary school mobility patterns if strike-induced education effects affect one's access to national labor markets. Relying on birth province rather than current province of residence in secondary school (table 8). We also find evidence of effect heterogeneity with respect to these outcomes on the family income dimension (table A8; tables A1-A10 are available online). 16 Primary school in Argentina comprises 1,260 instructional days (180 days per year). 17 We ignore national teacher strikes when constructing our treatment measure, as they are subsumed by the cohort fixed effects that we use. 18 The birth cohorts range from 1971 to 1985. These are the only cohorts that are between 30 and 40 years old when the outcomes are measured (2003-15) for which we can perfectly calculate exposure to teacher strikes during primary school. This means that we do not have a balanced panel of age observations across the EPH waves. In Sec. VI.C, we show that limiting our analysis to EPH waves 2011-15 for which we have a balanced panel has no impact on our results. Table 1 Days of Teacher Strikes During Primary School by Birth Cohort and Birth Province eliminates these endogenous migration issues. It is still the case that a fraction of respondents will be assigned the wrong treatment dose, as families can move across provinces such that birth province is different from the province in which the child attended primary education. However, table A1 shows that the province of residence is the same as the birth province for 93% of 13-year-olds in Argentina, and any bias resulting from this mobility is therefore likely to be very small. 19 To construct our analysis sample, we collapse the data on the birth province-birth year-EPH year level. Aggregation to this level is sensible because treatment varies on the birth province-birth year level. Table A2 provides summary statistics of the outcome variables that we use in our analysis. For educational attainment, we generate dummy variables for completion of secondary education and for having obtained at least a bachelor's degree. These indicators are constructed from a years of education variable that we also use to examine the educational attainment effect of strike exposure. With respect to labor market outcomes, we look at the proportion of people who are unemployed, out of the labor force, and dedicated to home production (neither studying nor working). To construct a measure of occupational skill, we follow Lovenheim and Willén (2019) and calculate the fraction of FIG. 2.-Data structure for a subsample of birth cohorts. A visual illustration of the data structure is shown for three cohorts that are part of our main analysis. workers in each occupation who have more than a high school degree. We use this to rank occupations by skill level to examine whether strike exposure leads individuals to sort into lower-skilled occupations. We also use the EPH measures of hours worked and earnings. Regarding earnings, we consider both the log of hourly wage and log of total labor earnings. 20 Since teacher strikes may affect labor force participation and unemployment, we also study the effect on the level of labor earnings, which includes individuals with zero earnings. 21 Preliminary evidence on the relationship between teacher strikes and student long-run outcomes is displayed in figure 3, which plots the predicted years of schooling (panel A) and labor income (panel B) as a function of the number of days of teacher strikes during primary school. 22 There is clear suggestive evidence of a strong linear negative correlation between teacher strikes and later-in-life outcomes: for each 180 days of teacher strikes (1 year of primary school), labor income is reduced by 6.7% and years of education decline by 3.1% relative to the sample means. 23 Though instructive, it is important to note that causal inference cannot be made from these graphs.
We also examine the effect of strikes on several sociodemographic outcomes: the likelihood of being the household head, the likelihood of being married, the number of children in the household, the age of the oldest child, the education level of the partner, and the per capita income of the household. In addition, we analyze intergenerational effects by examining the effect of teacher strikes on two education outcomes of children to individuals who were exposed to strikes in primary school. We first construct a dummy variable that equals one if the child is not delayed at school (age of the child minus years of education plus six is greater than zero). We then construct a variable of the educational gap of the child, defined by years of schooling plus six minus age. We collapse these variables at the household level.

C. Local Labor Market Controls
One of the main threats to our research design is the possibility that teacher strikes are driven by local labor market conditions, such that the effects that we identify do not represent the effect of exposure to teacher strikes during primary school holding all else constant but rather the effect 20 To prevent outliers from driving our results, we have trimmed the top and bottom percent of the hourly wage distribution. However, the results are robust to not performing this adjustment. 21 To account for potential selection bias influencing our wage and earnings effect, we follow Lee (2009) and estimate "worst-case scenario" treatment bounds. 22 The figures are obtained through a model that includes birth year, birth province, and EPH fixed effects. See the figure legend for information. 23 One hundred and eighty days is also the difference between the 10th and the 90th percentile of strike exposure among the individuals included in our sample.
FIG. 3.-Correlation between teacher strikes and student outcomes. The figures are binned scatterplots showing the correlation between teacher strikes and years of education (A) and teacher strikes and labor income (B). The horizontal axis shows the number of days of teacher strikes during primary school, which varies at the birth year-birth province level. The vertical axis shows the average years of education (A) and the average labor income (B) for each birth year-birth province-survey year cell, controlling for province, birth cohort, and survey year fixed effects. The data are divided into 20 equally sized groups based on days of strike exposure. Each point corresponds to the group average of the variable on the vertical axes. One hundred and eighty days of teacher strikes is equivalent to a full year of primary school (and the difference between the 10th and the 90th percentile of teacher strike exposure among the individuals included in our sample). of both teacher strikes and local labor market conditions during primary school.
To minimize this identification threat, we include two variables in our estimating equation that control for variation in local labor market conditions across provinces and time. First, we collect data on public administration strikes by province and year from CTI (the occupation with the largest number of strikes during our analysis period after teachers) and compute days of exposure to public administration strikes for each birth year-birth province cell during primary school. By controlling for public administration strikes, we exploit variation in teacher strikes net of any general province-specific events and conditions that fuel labor conflict. Second, we collect data on province-specific GDP. 24 We average the province-specific GDP during the 7 years of primary school for each birth year-birth province cell.
The local labor market controls reduce the risk that our results are driven by local labor market conditions; such factors have to be uncorrelated with province-specific GDP and public administration strikes and not absorbed by our fixed effects but are correlated with teacher strikes and independently affect the outcomes. One way in which this could happen is if teacher strikes are triggered by province-specific public school conditions. If, for example, poor material conditions or low salaries trigger strikes, and if these factors are not subsumed by our fixed effects and labor market controls, these factors could bias our results (as they could cause lower outcomes even if strikes had not occurred). To ensure that such factors are not driving our results, we have obtained data on teacher wages from the Ministry of Education. By showing that teacher wages are not related to strikes, we argue that our data are inconsistent with the idea that province-specific public school conditions drive our results.

D. Short-Run Outcomes
To examine whether the long-run effects that we identify are present immediately after the children have been subject to teacher strikes or whether the effects develop over time, we complement our main analysis with an analysis of the effect of teacher strikes on outcomes of students who have just finished primary school. 25 The data that we use for this analysis come from the 2003-15 EPH waves for children between 12 and 17 years old. We concentrate on educational outcomes since most of these individuals have not yet entered the labor market. These outcomes are the likelihood of having attended primary school, the probability of attending public school, years of education, the likelihood that the main activity is home production, and the likelihood of being enrolled in secondary school. Unfortunately, we do not have access to any test score data that can provide further evidence on the direct effect of teacher strikes on human capital accumulation. Though this analysis is useful for understanding the channels through which the long-run effects operate, it is important to note that this sample is different from our main analysis sample and that these individuals were exposed to teacher strikes in a time period different from our main analysis sample. Some caution is therefore encouraged when comparing the results from the two analyses.

V. Empirical Methodology
We exploit cross-cohort variation in exposure to teacher strikes during primary school within and across provinces over time in a dose-response difference-in-differences framework. Specifically, we estimate models of the following form separately for men and women: where Y pct is an outcome for respondents born in province p in birth cohort c and observed in EPH year t. Regressions are weighted by the number of observations in each birth province-birth year-calendar year cell. The variable of interest is TS_Exposure and measures the number of days (in tens of days) that the cohort was exposed to strikes during primary school. Standard errors are clustered on the birth province level. 26 Equation (1) includes province (J p ), birth cohort (ϑ c ), and calendar year (∅ t ) fixed effects, as well as a province-specific linear time trend (vT p ) and a cohort-specific linear time trend (dT c ). The province-specific linear time trend absorbs any trend in Y over time within a province, and the cohortspecific linear time trend absorbs any trend in Y over time within a birth cohort. Equation (1) further contains a vector of province-specific covariates (X pc ) that control for average socioeconomic and demographic characteristics of the province while the cohort was in primary school.
In addition to using equation (1) as defined above, we estimate models that substitute the time trends for birth province-by-calendar year and birth year-by-calendar year fixed effects. The birth province-by-calendar year fixed effects control for variation in Y that is common across birth cohorts within a province in a given year (e.g., province-specific macroeconomic shocks), and the birth year-by-calendar year fixed effects control for any systematic difference across birth years that may be correlated with exposure to teacher strikes and the outcomes of interest. Though more flexible than equation (1), this is a much more demanding specification, particularly bearing in mind our relatively low number of observations. However, our results are robust to which of these specifications that we use; results obtained from the more demanding specification are shown in table A3. 27 The unit of observation is birth province-birth year-calendar year, and the identifying variation stems from cross-cohort variation in exposure to teacher strikes during primary school within and across provinces. There are two main assumptions underlying our estimation strategy. First, that there are no shocks (or other policies) contemporaneous with teacher strikes that differentially affect the different cohorts. The most serious threat to this assumption is that strikes may be caused by political events or economic conditions that vary at the birth province-birth year level and independently affect the outcomes of interest. To limit this identification threat, we control for public administration strikes and provincial GDP during primary school. 28 These controls significantly reduce the risk that our results are driven by local conditions or secular shocks; such shocks would have to be uncorrelated with provincial GDP and public administration strikes but be correlated with teacher strikes and have an independent effect on our outcomes (and survive the fixed effects and linear time trends). We also use data on teacher wages to show that the data are inconsistent with the idea that our results are driven by province-specific public school conditions. 27 We also perform our analysis using an instrumental variable approach in which we instrument teacher strikes with public administration strikes. This strategy relies on assumptions that are distinct from those underlying our preferred method: that exposure to public administration strikes must be a good predictor of exposure to teacher strikes and that, conditional on the covariates and fixed effects included in the model, exposure to public administration strikes cannot have an independent effect on the outcomes of interest. The most serious threat to the exclusion restriction is that public administration strikes may have an effect on student outcomes that does not operate through exposure to teacher strikes (which is why we have included exposure to public administration strikes as a control variable in eq. [1]). However, given the rich set of fixed effects as well as the control for province-specific GDP that we include in our model, this is unlikely. Our main results are robust to this alternative approach. The main takeaway from this exercise is that-even if we cannot ascertain the validity of the assumptions underlying either of our two methods-the fact that our results are robust to which of these methods we use limits the sources of bias that can invalidate our results. The reason is that the two methods rely on completely different sets of assumptions. Results from the instrumental variable approach are available on request. 28 We do not possess information on provincial GDP for the city of Buenos Aires, and observations from the city of Buenos Aires are therefore not included in our baseline estimation. In panel A of table 7, we demonstrate that our results are robust to including the city of Buenos Aires (reestimating our preferred specification including observations from the city of Buenos Aires but excluding the provincial GDP control).
The second assumption underlying our analysis is that the timing of teacher strikes must be uncorrelated with prior trends in outcomes across birth cohorts within each province. The conventional method for examining the validity of this assumption is to estimate event-study models that nonparametrically trace out pretreatment relative trends as well as time-varying treatment effects. Our research design does not lend itself well to this approach, and we rely on two alternative methods for illustrating that the timing of teacher strikes is uncorrelated with prior trends in outcomes across birth cohorts within each province.
First, we incorporate province-specific linear time trends to show that our results are not driven by trends in outcomes across birth cohorts within each province. Second, we reassign the treatment variable for birth cohort c to birth cohort c-7, such that the measure of exposure to teacher strikes is the number of days (in tens of days) of primary school strikes that took place while the individuals were 13-19 years old. As these individuals have already completed primary school, they should be unaffected by these strikes, and the coefficient on TS_Exposure should not be statistically or economically significant. 29 It should be noted that a fraction of individuals in each birth provincebirth year-calendar year cell attended private primary school (18%), and it is unusual for private school teachers to participate in teacher strikes; while public teachers make up approximately 35% of all strikes in Argentina, private teachers account for less than 4% of all strikes (Chiappe 2011; Etchemendy 2013). As we assign treatment status based on public school teacher strikes, our point estimates will suffer a slight attenuation bias. 30

Educational Attainment
Panel A of table 2 presents gender-specific estimates of the effect of teacher strikes on educational attainment. Each cell in the table comes from a separate estimation of equation (1). Panel A provides strong evidence of adverse education effects associated with teacher strikes. Specifically, 10 days of strikes (0.79% of primary school) increase the number of both males and 29 The 13-19-year-olds may have been exposed to strikes as well (though this is unlikely given our discussion in Sec. IV.A). If strikes are correlated across years within provinces, this model may therefore produce economically and statistically significant results. This makes any null results even more powerful in supporting our identifying assumptions. 30 We could divide our estimates by the fraction affected by the strikes to obtain an approximation of the treatment-on-the-treated effect. However, since some private school teachers participate in strikes, we report the more conservative estimates without adjusting for take-up. females who do not graduate from high school by 30 out of every 1,000 and reduces the number of years of education by approximately 0.025. 31 These effects represent declines of 0.5% and 0.2% relative to the respective means, which are shown directly below the estimates in the table. With respect to tertiary education, we find that 10 days of strikes lead to an increase in the NOTE.-Authors' estimation of eq. (1) using 2003-15 Encuesta Permanente de Hogares (EPH) data on 30-40-year-old respondents who were born between 1971 and 1985. The unit of observation is birth province-birth year-EPH year, and the sample consists of 2,460 observations. Regressions include birth province, birth year, and EPH survey year fixed effects, as well as controls for local GDP and exposure to public administration strikes during primary school. Regressions further include a cohort-specific and a province-specific linear time trend. Regressions are weighted by the number of individual observations used to calculate the averages for each birth year-birth province-EPH year cell. The coefficient measures the effect of being exposed to 10 additional days of teacher strikes in primary school on the respective outcomes. Standard errors are clustered at the birth province level. * Significant at 10%. ** Significant at 5%. *** Significant at 1%. 31 Early-childhood investments are often argued to yield higher returns than investments that target older children, such that exposure to strikes in early grades may have larger effects. We explore this question in detail in Sec. VI.B. number of males who do not complete college with 24 out of every 1,000 but that it does not have an impact on females.
The average individual in our sample experienced 88 days of strikes during primary school. Scaling the point estimates to account for this level of exposure suggests that the average male (female) cohort suffered adverse effects with respect to the proportion obtaining a high school diploma, a college degree, and years of schooling equivalent to 4.75% (3.69%), 12.76% (2.82%), and 2.02% (2.02%), relative to the means. 32 These results demonstrate that teacher strikes not only have adverse short-term education effects (reduction in the proportion who obtain a high school diploma) but also impact the education decisions of individuals as they move up the education ladder (proportion who obtain a college degree and years of education). 33 This is an important finding that has not been documented before.

Employment, Labor Force Participation, and Home Production
Preexisting research has documented a strong positive relationship between educational attainment and labor market opportunities (e.g., Ashenfelter, Harmon, and Oosterbeek 1999;Card 1999;Harmon, Oosterbeek, and Walker 2003;Heckman, Lochner, and Todd 2006). 34 This suggests that teacher strikes may also affect students' labor market outcomes. Panel B of table 2 examines this question in detail, showing estimates for the proportion of individuals who are unemployed and not in the labor force and whose main activity is home production. Looking across the panel, there is clear evidence that strikes lead to an increase in the proportion of individuals who are unemployed: 10 days of strikes lead to an increase in the proportion of unemployed individuals by approximately one percentage point among both males and females (1.4% relative to the respective means). This demonstrates that the negative education effects of strike-induced school disruptions carry over to the labor market.
With respect to labor force participation, our results suggest that there is no statistically significant effect of exposure to teacher strikes on the probability of being a labor force participant. This suggests that school disruptions caused by teacher strikes have an impact on the intensive margin of 32 This rescaling assumes linear treatment effects. Given the suggestive evidence in fig. 3, this is not an unreasonable assumption. 33 In Sec. VI.D, we study the effect of teacher strikes on contemporaneous educational outcomes for children aged 12-17, something that we cannot do for our main analysis sample due to data limitations. This auxiliary analysis reveals negative educational effects consistent with the results for older cohorts discussed in this section. 34 However, it is not necessarily the case that adverse educational effects carry over to the labor market (e.g., Böhlmark and Willén, forthcoming). employment but that it does not necessarily change the composition of workers that make up the labor force. 35 Finally, the results in panel B of table 2 also show that strikes increase the proportion of people whose main activity is home production, though this effect is statistically significant only among females. 36 In terms of effect size, the results suggest that 10 days of strikes move 30 out of every 1,000 females into home production. The male estimate is smaller but not statistically significantly different.

Earnings and Wages
The adverse employment and education effects identified in table 2 suggest that teacher strikes may negatively impact earnings and wages as well. This is examined in panel C of table 2 with respect to log earnings, log wages, and the level of earnings. The results show that both males and females experience reductions in log wages. The table also shows that strikes reduce total earnings of females but not males. However, in terms of effect sizes, the gender-specific estimates are not statistically significantly different from each other. In terms of magnitudes, the results indicate that 10 days of strikes lead to a reduction in male earnings by 0.2% (log specification), wages by 0.3%, and total earnings by $1.8 (level specification). For females, the numbers are 0.2%, 0.2%, and $1.9. Scaling the point estimates to account for the average level of exposure to strikes suggests that men (women) in our sample suffered adverse effects of 1.85% (1.94%), 2.82% (1.67%), and 2.02% (4.49%), respectively. 37 35 It is worth noting that if we control for province-specific linear birth year trends (as in panel F of table 7), we do find significant negative labor force participation effects among women (exposure to 10 days of strikes reduces female labor force participation by 0.14% relative to the mean). Our inability to detect this effect in our baseline table may therefore be due to secular shifts in labor market opportunities that occurred for women over the cohorts that we consider (Blau and Kahn 2013;Gasparini and Marchioni 2015;Bick et al. 2019). 36 This effect is driven by a slight fall in labor force participation (not statistically significant) combined with a decline in university enrollment. It is not unusual in Argentina to be enrolled at a university after the age of 30. 37 It is worth pointing out that the wage/earnings effects that we identify may be driven by changes on both the intensive and the extensive margin due to the employment effects identified in table 2. To overcome this problem, we have used the trimming procedure for bounding treatment effects in the presence of sample selection (in this case, bounding the wage and earnings effects due to the potential selection problem caused by the fact that strikes also impact employment) developed by Lee (2009). To implement this bounding procedure, we first identify the excess number of individuals selected out of the earnings/wage sample because of treatment (identified through our negative employment effect) and then trim the upper and lower tails of the outcome (log wage and log earnings) distributions of each birth year-birth province-survey year cell according to this number multiplied by teacher strikes. This provides us with a worst-case scenario bound. Since One way to interpret the wage effect that we identify is to aggregate it up to the country level and consider the total effect on the economy. While such back-of-the-envelope calculations must be cautiously interpreted, it is informative for understanding the potential magnitude of the effect. Using the point estimates on log wage, we calculate that the annual earnings loss induced by strikes amounts to $2.34 billion. 38 This is equivalent to the cost of raising all primary school teacher wages in Argentina by 62.4%, suggesting that it may be worth raising teacher wages if it will prevent them from going on strike. 39 The point estimates in panel C of table 2 suggest that the return to education in Argentina is about 6%. 40 This estimate is slightly lower than the preexisting estimates in Argentina of 7%-12.5% (Kugler and Psacharopoulos 1989;Pessino 1993Pessino , 1996Galiani and Sanguinetti 2003;Patrinos, Fiszbein, and Giovagnoli 2007;Gasparini et al. 2011a). However, it is important to note that school missed due to sporadic school closures is fundamentally different than less schooling because one leaves school at an earlier age. In one case curriculum and learning is repeatedly interrupted, and in the other it is not. As such, human capital accumulation might be very different and hence the estimated "return" to years of schooling could be very different. 41 It is not clear how much one would want to extrapolate from our estimates about returns to schooling that is more general than the impact of disrupted education. Nevertheless, this type of comparison helps anchor our estimates and put the effects in relation to more known education interventions. the employment effect is relatively modest for males, this exercise does not have a large effect on our estimates and the bounds are very tightly estimated. We find larger bounds for females, consistent with larger employment effect, but the upper bound is always negative, indicating that not all of the effect on earnings is driven by the extensive margin. Specifically, for log earnings we obtain a lower bound of 20.0039 and an upper bound of 20.0026 for males (20.0045 and 20.0012 for females), and for log wages we obtain a lower bound of 20.0031 and an upper bound of 20.0017 for males (20.0045 and 20.0006 for females). 38 To obtain this number, we first multiply the gender-specific wage effects with the total gender-specific labor income for the country (using 2014 EPH data). We then add these two numbers together and scale the sum by the average treatment exposure (88 days). The result is interpreted as the total earnings loss for the Argentinean economy if all employed workers were exposed to the average treatment, assuming that the gender-specific effects on earnings are constant across age groups. 39 Teacher wages are approximately $13,000 a year, and there were 289,812 primary school teachers in 2014.
The wage and earnings results in table 2 may conceal important heterogeneous effects across the earnings and wage distributions. We explore this possibility in table 3 with respect to total earnings (panel A) and log wages (panel B). The results in panel B demonstrate that strikes affect all but the tails of both the male and the female wage distributions. The magnitude of the effect is relatively constant across the different deciles. These results indicate that people in the left tail of the wage distribution would have done equally poorly without strikes and that people in the right tail of the wage distribution would have done equally well without strikes, while the rest of the individuals would have done better. With respect to total earnings, our results are again very similar across men and women.
To better understand the pattern of these wage and earnings results, panel C shows results from a similar heterogeneity analysis with respect to educational attainment. These results largely mirror the wage and earning results in the sense that there are statistically significant and adverse effects across almost all deciles of the distribution and that the magnitude of the effect is relatively constant across the different deciles.

Occupational Quality, Informal Employment, and Hours Worked
In addition to the extensive margin employment effects that we identify above, the adverse effect of strikes on earnings could be driven by a reduction in work hours or by worse employment conditions. This is examined in panel D of table 2, where we look at occupational sorting, hours worked, and the proportion that work in the informal sector.
The results show that being exposed to 10 days of strikes in primary school has no effect on hours worked, but it does have a large negative effect on occupational sorting among men. 42 This effect is not present among women, and we can reject the null hypothesis that there is no difference in effect size across genders. With respect to the average male who was exposed to 88 days of teacher strikes during primary school, the occupational sorting effect represents an effect of 7.48% relative to the sample mean.
With respect to the likelihood of working in the informal sector, we find a precise null effect among males but a sizable effect among females. Although the coefficient falls just outside of being statistically significant at conventional levels, the estimate is much larger than its standard error, and in alternative specifications where we include province-specific linear cohort trends (panel F of table 7) or where we replace the time trends with two-dimensional fixed effects (table A3), we find statistically significant effects. We cautiously interpret this as indicative of an effect on the likelihood of working in the informal sector among females. For the average female in our sample who was exposed to the 88 days of teacher strikes during primary school, the increase in the likelihood of working in the informal sector represents an effect of 4.2% relative to the mean.

Socioeconomic and Intergenerational Effects of Teacher Strikes
There is a large literature documenting a strong positive relationship between an individual's education and labor market outcomes and his or her socioeconomic position (e.g., Finer and Zolna 2014). Teacher strikes may therefore also impact outcomes such as the likelihood of being married, the probability of being the head of the household, fertility, the educational attainment of the partner, and per capita household income. 43 Table 4 shows results from estimation of equation (1) for each of these outcomes. Table 4 shows that strikes affect the characteristics of the partners of the individuals who are exposed to teacher strikes. Specifically, the results show that the partners of females who were exposed to strikes are less educated, such that females experience a marriage downgrade with respect to partner skill: being exposed to the average level of strikes during primary school leads to a decline in the years of education of females' partners by 4.7% relative to the sample mean. We do not find a significant effect among males. In addition to marriage downgrading, the point estimates in table 4 show that strikes affect per capita family income: the average individual in our sample is exposed to 88 days of teacher strikes, and this is associated with a decline in per capita household income by around 4.0% relative to the sample mean. The effect is not statistically significantly different across genders. 44 There are no statistically significant effects on the likelihood of being married, the probability of being the head of the household, or the outcomes regarding fertility decisions.
Given that strikes have adverse effects on student education and labor market outcomes and also influence other sociodemographic outcomes, there may be intergenerational effects associated with strikes. This question is explored in table 5, using the intergenerational outcome variables discussed in Section IV as dependent variables. Across the table, there is evidence of adverse intergenerational education effects among females but not males. In terms of magnitude, being exposed to 10 days of strikes in primary school leads to a 0.43% increase in the probability that the child is delayed at school and to an increase in the education gap of 1.45% relative to the respective means. These results have not been documented before, and additional research that examines these questions should be encouraged. 43 Given the structure of the EPH, we can identify only children of the head of the household or the spouse of the head of the household. 44 The point estimate on per capita family income is identified based off changes in the labor earnings of the individuals exposed to strikes as well as off changes in the labor earnings of their partners and household's composition. unit of observation is birth province-birth year-EPH year, and the sample consists of 2,460 observations. Regressions include birth province, birth year, and EPH survey year fixed effects, as well as controls for local GDP and exposure to public administration strikes during primary school. Regressions further include a cohort-specific and a province-specific linear time trend. All outcomes are expressed in 2005 purchasing power parity dollars. The percent effect is dropped for log wage and log earnings, as the point estimates are already interpreted as a percentage change. Regressions are weighted by the number of individual observations used to calculate the averages for each birth year-birth province-EPH year cell. The coefficient measures the effect of being exposed to 10 additional days of teacher strikes in primary school on the respective outcomes. Standard errors are clustered at the birth province level. * Significant at 10%. ** Significant at 5%. *** Significant at 1%.

B. Heterogeneous Treatment Effects
A large literature has documented that human capital accumulates over time, such that human capital obtained at one point in time facilitates further skill attainment later in life (e.g., Heckman, Lochner, and Todd 2006). Therefore, early childhood investments are often argued to yield higher returns than education investments that target older children. 45 With respect to the current analysis, this suggests that exposure to strikes in early grades may have larger adverse effects on long-run educational and labor market outcomes. Table 6 shows the differential effect of strikes in grades 1-4 and 5-7 on the long-term education and labor market outcomes. The table provides some evidence that the effects are stronger if strikes occur in early grade years: even though the point estimates on strikes in later grade years oftentimes are not statistically significantly different from the point estimates on strikes in earlier grade years, the standard errors are generally larger such that many of the effects are statistically significant only in early grades. With respect to the magnitude of the effects, we find for only two outcomes that the effect of teacher strikes in early school grades is statistically significantly different from the effect of teacher strikes in later school grades: years of education and total earnings for females. (1) using 2003-15 Encuesta Permanente de Hogares (EPH) data on 30-40-year-old respondents who were born between 1971 and 1985. The unit of observation is birth province-birth year-EPH year, and the sample consists of 2,460 observations. Regressions include birth province, birth year, and EPH survey year fixed effects, as well as controls for local GDP and exposure to public administration strikes during primary school. Regressions further include a cohort-specific and a province-specific linear time trend. Educational attainment of the partner is defined for heads of households or spouses to heads of households. Regressions are weighted by the number of individual observations used to calculate the averages for each birth year-birth province-EPH year cell. The coefficient measures the effect of being exposed to 10 additional days of teacher strikes in primary school on the respective outcomes. Standard errors are clustered at the birth province level.
** Significant at 5%. *** Significant at 1%. (1) using 2003-15 Encuesta Permanente de Hogares (EPH) data on 30-40-year-old respondents who were born between 1971 and 1985. The unit of observation is birth province-birth year-EPH year, and the sample consists of 2,460 observations. Regressions include birth province, birth year, and EPH survey year fixed effects, as well as controls for local GDP and exposure to public administration strikes during primary school. Regressions further include a cohort-specific and a province-specific linear time trend. Not being delayed at school is a dummy variable that takes the value of one if the age of the child minus years of education plus six is greater than zero. The educational gap is defined as years of schooling plus six minus age. Regressions are weighted by the number of individual observations used to calculate the averages for each birth year-birth province-EPH year cell. The coefficient measures the effect of being exposed to 10 additional days of teacher strikes in primary school on the respective outcomes. Standard errors are clustered at the birth province level. *** Significant at 1%. (1) using 2003-15 Encuesta Permanente de Hogares (EPH) data on 30-40-year-old respondents who were born between 1971 and 1985. The unit of observation is birth province-birth year-EPH year, and the sample consists of 2,460 observations. Regressions include birth province, birth year, and EPH survey year fixed effects, as well as controls for local GDP and exposure to public administration strikes during primary school. Regressions further include a cohort-specific and a province-specific linear time trend. Regressions are weighted by the number of individual observations used to calculate the averages for each birth year-birth province-EPH year cell. The coefficients measure the effect of being exposed to 10 additional days of teacher strikes in grades 1-4 and grades 5-7 on the respective outcomes. Standard errors are clustered at the birth province level. * Significant at 10%. ** Significant at 5%. *** Significant at 1%.
Another source of heterogeneity concerns the fact that the effect of several short disruptions may be very different from the effect of one long disruption. Unfortunately, the strike data that we have collected provide us with only the number of days of strikes (and the number of strikes) per month and province (not the length of each individual strike). However, even if we cannot identify the duration of each strike, the data allow us to identify the average duration of the strikes that each cohort was exposed to. To obtain suggestive evidence of effect heterogeneity with respect to disruption type, we have therefore estimated our main specification with the continuous treatment measure of strike exposure but also included a variable that accounts for the average duration of the strikes that the cohort was exposed to (calculated as the total number of days of strikes divided by the total number of strikes). The results from this exercise are shown in table A10. Looking across the table, we find no evidence that the average duration of the strikes that the cohort was exposed to has an impact on the long-run outcomes that we look at independently off the effect of the number of days of strikes. However, the inclusion of this variable strengthens our main results with respect to both magnitude and statistical significance.

C. Robustness and Sensitivity Analysis
The results obtained from our preferred specification support the idea that school disruptions caused by teacher strikes have adverse effects on long-term educational attainment and labor market outcomes. In this section, we explore evidence on whether these results are driven by other policies, trends, or events that are not accounted for by the controls in equation (1).
In panel A of table 7, we include the city of Buenos Aires, and in panel B we exclude the province of Buenos Aires. 46 These large geographic areas may systematically be very different from the rest of Argentina, and the purpose of this exercise is to ensure that our results are not exclusively driven by these geographic areas. The results are robust to these adjustments.
In panel C, we estimate equation (1) without the five provinces that have the highest cross-province mobility rates. 47 The point estimates produced for this subsample of provinces are not statistically significantly different from our baseline results. This demonstrates that our results are robust to accounting for cross-province mobility.
Panel D eliminates pre-2010 EPH survey years to ensure that our results are robust to a balanced panel of age observations. Despite a dramatic loss of observations (recall that our baseline analysis relies on the 2003-15 EPH waves), the point estimates are not statistically significantly different from our baseline results when imposing this restriction.
Panel E displays results from estimation of equation (1) when we have reassigned treatment for birth cohort c to birth cohort c-7. These cohorts are very close in age and are likely exposed to similar province-specific macroeconomic environments. However, the c-7 cohorts have already completed primary school when the documented teacher strikes took place, and if our baseline estimates successfully isolate the effect of teacher strikes on student outcomes, we should not find any statistically significant effects among these cohorts. None of the point estimates are statistically significant; the results are consistent with the assumption that the strikes are uncorrelated with trends in outcomes across birth cohorts within each province.
Panel F shows results for our preferred specification when provincespecific linear birth year trends have been included. These results help us examine whether the estimates are simply driven by trends in outcomes across birth cohorts within each province. The results from this exercise are not statistically significantly different from our baseline estimates.
One concern with our analysis is that the results may not be driven by adverse effects of teacher strikes on the outcomes of exposed students but rather by positive effects of teacher strikes on future student cohorts (both of these stories would produce a negative difference-in-differences estimator). This would be true if, for example, strikes have no impact on exposed students but the ability of teachers to strike gives them leverage in negotiations, leading to changes in working conditions that attract a different quality of teachers or affect investments in schooling in a way that benefits future students. To examine this threat to identification, panel H of table 7 shows results obtained from reestimating our baseline equation using exposure to strikes prior to start of school as our treatment variable (when the students are between 0 and 4 years old). If teacher strikes affect future student outcomes, we would expect this analysis to return significant results. The reason is that strikes that took place before the individuals started school cannot affect their time in school. However, if, for example, teacher strikes positively affect working conditions, strikes can have an impact on the education quality that these individuals experience when they start school. All point estimates are small and not statistically significant, suggesting that our data are inconsistent with this idea.
One of the main threats to valid inference in our paper is that our results are simply picking up differences in outcomes caused by province-specific variation in macroeconomic performance across time. To explore this question, we use post-2003 EPH data (data on local labor markets do not exist before 2003) to examine the relationship between teacher strikes and local labor market conditions. The results from this exercise are shown in table A6. In column 1, we show the correlation between teacher strikes and the unemployment rate, the average hourly wages, and the average per capita family income. In column 2, we add days of public administration strikes, calendar year, and province fixed effects, as well as province-specific time trends. 48 Once we add these controls, there is no relationship between the local labor market climate and teacher strikes. NOTE.-Authors' estimation of eq. (1) using 2003-15 Encuesta Permanente de Hogares (EPH) data on 30-40-year-old respondents who were born between 1971 and 1985. The unit of observation is birth provincebirth year-EPH year, and the sample consists of 2,460 observations. Regressions include birth province, birth year, and EPH survey year fixed effects, as well as controls for local GDP and exposure to public administration strikes during primary school. Regressions further include a cohort-specific and a provincespecific linear time trend. Panel A excludes the city of Buenos Aires. Panel B excludes both the city and the province of Buenos Aires. Panel C excludes the five provinces with the highest cross-province mobility rates (Chaco, Corrientes, Misiones, Rio Negro, and Santa Cruz). Panel D eliminates pre-2010 EPH survey years to obtain a balance panel. Panel E shows results from the falsification test where we have reassigned the treatment variable for cohort c to cohort c-7. Panel F incorporates province-specific linear birth year trends to the estimation of eq. (1). Panel G drops the top 1% of the teacher strike exposure distribution. Regressions are weighted by the number of individual observations used to calculate the averages for each birth year-birth province-year. Panel H looks at the effect of teacher strikes when the individual was between 0 and 4 years using 30-37-year-old respondents who were born in 1980-85 (since we do not have strike information for older cohorts during their first years). The coefficient in panels A-G should be interpreted as the effect of being exposed to teacher strikes for 10 extra days during primary school. The coefficient in panel H should be interpreted as the effect of being exposed to teacher strikes for 10 extra days when between 0 and 4 years old. Standard errors are clustered at the birth province level. * Significant at 10%. ** Significant at 5%. *** Significant at 1%. 48 The results are robust to the inclusion of the 30th and 70th percentiles of the per capita family income (intended to capture any effect of a change in the distribution of per capita family income). Results are available on request.
Even if our results are not driven by province-specific variation in macroeconomic performance over time, it could still be the case that provincespecific public school conditions are driving the results (e.g., poor material conditions or low wages). If such school conditions are correlated with teacher strikes but not absorbed by our fixed effects, time trends, or local labor market controls, they may contaminate our effects, as these conditions could have led to lower outcomes of exposed cohorts even if strikes did not happen. To explore this possibility, we look at the relationship between teacher strikes and teacher wages.
The results from this exercise are shown in table A7. In column 1, we show the correlation between teacher wages and strikes. In column 2, we add controls for public administration strikes as well as calendar year and province fixed effects. There is no significant relationship between teacher wage and teacher strikes. These results suggest that our results are not driven by province-specific public school conditions across time. 49

D. Short-Run Effects
In this section, we analyze the effect of teacher strikes on students who have just finished primary school. 50 The purpose of this exercise is to examine whether the strike effects occur immediately after the children have experienced school disruptions or if they develop over time. We focus on children between 12 and 17 years old when performing this analysis. 51 We concentrate on educational outcomes since most of these individuals have not yet entered the labor market. These outcomes are the likelihood of having attended primary school, the probability of attending a public institution, years of education, the likelihood that the main activity is home production, and the likelihood of being enrolled in school. We perform this analysis on the individual level to control for household characteristics. 52 Table 8 displays the results for each of the above outcomes using two different specifications. Column 1 incorporates the same controls as in our preferred specification. 53 Column 2 incorporates additional local labor market controls (the unemployment rate and the average wage in each provinceyear) and family characteristics. 54 With respect to females, the results in table 7 show that there is a decline in public education enrollment of 0.93% relative to the mean. This represents a 5.3% decline after scaling the coefficient to account for the average level of strikes among these individuals (57 days). We also find an increase in the likelihood of home production by 3.45% and a decrease in the probability of being enrolled by 4.02%. For males, exposure to strikes reduces the years (1) using 2003-15 Encuesta Permanente de Hogares (EPH) data on 12-17-year-old respondents. Column 1 shows results using individual-level data and the same controls as in our baseline specification. The specification used to produce the results in col. 2 incorporates local labor market variables that may influence the wealth of the family: the unemployment rate and the average wage in each province. It further includes four dummies of province-specific quartiles of per capita family income and five dummies for the maximum educational level of the head or spouse of the household (primary education or less, incomplete secondary, complete secondary, incomplete tertiary, and complete tertiary). Public education is a dummy variable equal to one if attending a public school. Home production is a dummy that equals one if the respondent is neither working nor studying. Standard errors are clustered at the birth province level. The coefficients are interpreted as the effect of being exposed to teacher strikes for 10 extra days during primary school. * Significant at 10%. ** Significant at 5%. 53 Except for GDP at the province level, for which there are no reliable data available in recent years. 54 Four dummies for province-specific quartiles of per capita family income and five dummies for the maximum educational level of the head of the household: primary education or less, incomplete secondary, complete secondary, incomplete tertiary, and complete tertiary. of education by 0.29% relative to the mean. These results suggest that the negative education effects are visible immediately after the students finish primary school. The short-run effects being smaller than the long-run effects (table 2) is consistent with the total effect of teacher strikes during primary school becoming more noticeable when all education decisions have been made.
In Section II.C, we note that there may be heterogeneous treatment effects of teacher strikes with respect to the socioeconomic characteristics of the student's parents: wealthy parents can afford to move their children to private institutions if they believe that the strikes hurt their children, and more educated parents are more likely to be capable of replacing lost instructional days with home schooling. Even though we do not have information on parental wealth and educational attainment for the individuals included in our main analysis, we can examine this for children who are between 12 and 17 years old. In table A8, we estimate the effect of strikes by per capita family income and maximum years of education of the head of the household. Consistent with our predictions, we find evidence that the most affected students are those from the most socioeconomically disadvantaged households.

VII. Discussion and Conclusion
Teacher industrial action is a prevalent feature of public education systems across the globe. Despite a large theoretical literature on labor strikes and a reignited debate over the role of teachers' unions in education, there is a lack of empirical work that evaluates the effect of teacher strikes on student outcomes. This paper contributes to the literature by providing a detailed analysis of the effect of teacher strikes on long-run education and labor market outcomes. This is not a full analysis of the benefits and costs associated with teacher strikes but rather a partial equilibrium analysis that uses teacher strikes to measure the effect of school disruptions on student long-term outcomes.
Our results identify adverse long-run educational and labor market effects for both males and females. For males, we find that school disruptions fueled by teacher strikes lead to a reduction in educational attainment, an increase in the likelihood of being unemployed, occupational downgrading, and adverse effects on both labor market earnings and hourly wages. The effects are very similar for females, with the exception that there is no effect on occupational sorting. Rather, there is an increase in the probability of engaging in home production. By looking at 12-17 years old, we demonstrate that the negative educational effects are visible immediately after children have finished primary school and that these effects are concentrated among children from the most vulnerable households. Our analysis reveals that strikes affect individuals on other socioeconomic dimensions as well. Specifically, individuals exposed to teacher strikes have less educated partners and lower per capita family income. We also find adverse intergenerational effects on their children.
The prevalence of teacher strikes in Argentina means that the effect on the economy as a whole is substantial: a back-of-the-envelope calculation amounts to an aggregate annual earnings loss of $2.34 billion. This is equivalent to the cost of raising the average employment income of all primary school teachers in Argentina by 62.4%. This suggests that it may be worth raising teacher wages if this will prevent them from going on strike.
Taken together, our results stress the importance of stable labor relations between government and industry and emphasize the necessity of a good bargaining environment that reduces the number of strikes that students are exposed to. Given that the negative effects that we identify last for years and even generations, it could generate substantial benefits if both unions and government attempt to limit the prevalence of strikes.