Education Curriculum and Student Achievement: Theory and Evidence

Andrietti, Vincenzo; Su, Xejuan Working Paper Education Curriculum and Student Achievement: Theory and Evidence UC3M WP Economic Series, No. 16-07 Suggested Citation: Andrietti, Vincenzo; Su, Xejuan (2016) : Education Curriculum and Student Achievement: Theory and Evidence, UC3M WP Economic Series, No. 16-07, Universidad Carlos III, Madrid, https://hdl.handle.net/10016/22883 , https://hdl.handle.net/10016/22883 This Version is available at: https://hdl.handle.net/10419/140619 Standard-Nutzungsbedingungen: Die Dokumente auf EconStor dürfen zu eigenen wissenschaftlichen Zwecken und zum Privatgebrauch gespeichert und kopiert werden. Sie dürfen die Dokumente nicht für öffentliche oder kommerzielle Zwecke vervielfältigen, öffentlich ausstellen, öffentlich zugänglich machen, vertreiben oder anderweitig nutzen. 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If the documents have been made available under an Open Content Licence (especially Creative Commons Licences), you may exercise further usage rights as specified in the indicated licence. http://creativecommons.org/licenses/by-nc-nd/3.0/es/ Working Paper Departamento de Economía Economic Series 16-07 Universidad Carlos III de Madrid April 2016 C/Madrid, 126 28903 Getafe (Spain) ISSN 22340-5031 Fax (34-91) 6249875 Education Curriculum and Student Achievement: Theory and Evidence* Vincenzo Andrietti† Xuejuan Su‡ Abstract This paper proposes a theory of education curriculum and analyzes its distributional impact on student learning outcomes. Different curricula represent horizontal differentiation in the education technology, thus a curriculum change has distributional effects across students. We test the model using the quasi-natural experiment of the G8 reform in Germany. We find evidence of heterogeneous reform effects consistent with our theory. While the reform improves student test scores on average, such benefits are more pronounced for well-prepared students. In contrast, less-prepared students do not benefit from the reform. JEL Classification: I21, I28, D04 Keywords: Education curriculum, horizontal differentiation, distributional effects, difference-in- differences, conditional quantile regression, unconditional quantile regression *Acknowledgments: We are grateful to Nicole Fortin for sharing the STATA codes with us. We thank seminar participants at the University of Alberta for their helpful comments. All remaining errors are our own. † Università “G. d'Annunzio” di Chieti e Pescara, DiSFPEQ. E-mail: [email protected] ‡ University of Alberta, Department of Economics. E-mail: [email protected] 1 Introduction Students of different levels of preparation (or prior knowledge) have different learning needs. Given the hierarchical nature of a learning process, students need to comprehend, apply, and synthesize the basic materials before they can effectively learn more advanced ones. In other words, their human capital output from an earlier stage of learning becomes the input and determines the learning effectiveness at a subsequent stage. As a result, wellprepared students – i.e., those with good prior knowledge or, equivalently, high human capital output from previous learning – can learn new topics more quickly, while lessprepared students – i.e., those with poor prior knowledge – need remedial work on the old materials before they can embark on the new ones, so they learn the new topics more slowly. In this sense, when the pace of learning is ideally matched to a student’s preparation, her learning effectiveness will improve, leading to better learning outcomes. To capture this concept of an ideal match between the pace of learning and the preparation of a student, we propose a theoretical model of the education curriculum. More specifically, an education curriculum is characterized by two parameters: a progress rate, and a corresponding minimum threshold on student preparation. A more challenging curriculum is one with a fast progress rate and a high threshold, while a less challenging curriculum is one with a slow progress rate and a low threshold. Given different curriculum options, well-prepared students enjoy better learning outcomes under a more challenging curriculum, while the opposite is true for less-prepared students. Thus, different curricula represent “horizontal differentiation” in the education technology, and the “ideal” curriculum – namely, the one that maximizes a student’s learning effectiveness – differs across students depending on their preparation levels. The horizontal feature of the education curriculum stands in sharp contrast to other important factors of the education technology, which have been extensively studied in the literature. Many of those factors represent “vertical differentiation” in the education technology, so students share similar preferences when given different options. For example, school resources, class size, teacher quality (or teacher experience), and peer effects are all vertical features of the education technology. Since more resources, smaller clas- 1 ses, better teachers, and better peers all contribute to better learning outcomes, when given a choice, all students will prefer to have higher quality (along these dimensions) to lower quality, everything else the same. Unlike these vertical quality dimensions, not all students prefer to have a more (or less) challenging curriculum. Instead, they prefer different curricula depending on their preparation levels. An immediate implication of the horizontal feature of the education curriculum is its distributional impact across students. When a number of students are subject to the same education curriculum, for example, because they live in the same state, attend the same school, or share the same class, the curriculum adopted in that state, school, or class applies to all of them despite their different preparation levels. Except for a lucky few where the match happens to be ideal, mismatches are likely to happen to many of the students. In particular, an over-match arises when the curriculum is too fast-paced (and accordingly imposes too high a threshold) for a student, and an under-match arises when the curriculum is too slow-paced for a student. Both types of mismatches are detrimental to the learning effectiveness of the students, and the more severe the mismatch, the more harm on their potential learning outcomes. The most extreme mismatches can be mitigated when a student repeats a grade (extreme over-match) or skips a grade (extreme under-match). However, moderate mismatches are likely to persist given that it is all but infeasible to individually customize the education curriculum to ideally suit each student’s learning needs. As a consequence, when there is a change in the education curriculum, there is similar distributional impact across students. For example, when the new curriculum is more challenging than the old one, it gets closer to the ideal curriculum for the well-prepared students, but farther away from that for the less-prepared students. As a result, wellprepared students benefit from the change and enjoy better learning outcomes, while the opposite is true for less-prepared students. In this sense, a curriculum change generates heterogeneous effects on student learning outcomes, and the relationship is monotonic in student preparation levels. More specifically, the relationship is monotonically increasing when the new curriculum is more challenging, and monotonically decreasing when the 2 new curriculum is less challenging. We empirically test this model. More specifically, we are interested in finding out whether a curriculum change has heterogeneous effects on student learning outcomes, and whether the pattern of the heterogeneous effects is consistent with the theory. There are two major challenges in our empirical analysis. The first is that education curriculum, as characterized by the two parameters, is not directly measurable in the data. While most teachers intuitively adjust their pace of teaching to better serve their students (e.g., slowing down and doing a few extra practice questions when students seem to struggle with a topic), it is difficult to assign a numerical value to reflect such curriculum adjustment in practice. As a first step, we circumvent this problem by focusing on the ordinal rather than the cardinal comparison between two curricula: Namely, determining which curriculum is more challenging without deciding by how much. The second challenge is that education curriculum, as actually adopted by educators, is necessarily an endogenous choice. This choice naturally depends on both the distribution of student preparation and the objective function of the educator, both of which may be unobserved in the data. In this sense, cross-sectional variation of observed curricular differences can be confounded by important unobserved factors, making it unsuitable for identification purposes. We deal with this problem by relying on a quasi-natural experiment of the curriculum change. For our empirical analysis, we take advantage of the G8 reform in Germany. This reform – implemented from 2001 to 2008 in most German states – compressed high school for the academic-track (Gymnasium) students from nine to eight years, while keeping the academic content required for graduation fixed. Namely, the reform requires the same amount of content being covered in a shorter time period, implying a faster progress rate and, accordingly, a higher preparation threshold. Thus, compared to the control (G9) states, the treated (G8) states have a more challenging curriculum. Furthermore, the G8 reform can be viewed as a quasi-natural experiment. It was implemented by states based mainly on considerations of the labor market conditions and demographic changes, with little focus on student learning outcomes directly. In this sense, the G8 reform can be viewed as an exogenous curriculum change, which allows us to identify the distributional 3 effects on student learning outcomes. To measure student learning outcomes, we use five waves of PISA data containing their reading, mathematics, and science test scores at the end of the ninth grade. Since the pooled PISA data are repeated cross-sections rather than panel data, we have very limited information on student preparation when they entered high school. Two approaches are used in the empirical analysis. The first is the conventional difference-in-difference (DiD) approach, where time- and state-variation in the G8 reform implementation allow us to identify the average effect of the curriculum change. More importantly, we use some crude measure of student preparation to interact with the reform variable, and estimate the heterogeneous effects of the curriculum change as distinct average effects for two subgroups of students, the well-prepared and the less-prepared. The second is a quantile treatment effect approach, where we rely on distributional assumptions of the unobserved preparation variable. In particular, we use both the conventional quantile regression method (conditional quantile regression) and the recentered influence function method (unconditional quantile regression) in a nonlinear DiD setting. The results can be interpreted as the treatment effects at different quantiles of either the conditional distribution or the unconditional distribution of test scores respectively. The empirical evidence is broadly consistent with our theoretical predictions. While the G8 reform improves student test scores on average, the benefits are more pronounced for well-prepared students. In contrast, there is little evidence that less-prepared students benefit from the reform at all. The rest of the paper is structured as follows. Section 2reviews the related literature. Section 3introduces the theoretical model of education curriculum and derives the model predictions. Section 4presents the regression models that empirically test the theoretical predictions. Section 5illustrates the natural experiment and the data exploited for the empirical analysis. Results are presented in Section 6. Section 7offers concluding remarks. 4 2 Related literature This paper is linked to several strands of the existing literature. On the theoretical side, there is a growing literature that focuses on the hierarchical nature of the education process, namely the human capital output from an earlier stage is an input for human capital accumulation and improves the learning effectiveness at a subsequent stage of education (see, for example, Ben-Porath,1967;Lucas,1988;Driskill and Horowitz,2002;Su,2004, 2006;Blankenau,2005;Blankenau et al.,2007;Cunha and Heckman,2007;Gilpin and Kaganovich,2012). More specifically, a few of these studies (Su,2004,2006;Gilpin and Kaganovich,2012;Kaganovich and Su,2015) focus on the role of a curricular threshold as an important determinant in the education technology, and derive the implications of such a threshold on the aggregate efficiency and distributional equality.1 The paper is also related to the literature on how peer effects affect students’ school choices and learning outcomes (see, among others, Rothschild and White,1995;Winston, 1999;Epple and Romano,1998,2008;Epple et al.,2002,2004,2006). The peer effects literature captures a vertical feature of the education technology, namely the higher is the average quality of one’s peers, the better off is a student in terms of her learning outcomes. Such a peer effect captures the “direct” externality that peers exert on a student’s learning. In contrast, our paper focuses on the “indirect” peer effect: that is, one education curriculum is adopted to serve both the student and her peers. So even if the student does not directly benefit from having high-quality peers, he is nonetheless affected by the adopted education curriculum, which may be chosen to better serve her peers rather than himself. The two kinds of peer effects have drastically different implications. While the direct peer effect suggests that all students would prefer to have as high quality peers as possible, the indirect peer effect suggests that this is not necessarily optimal. For example, if a low ability (or less prepared) student were to attend a school with predominantly high ability (or well prepared) students, he would find its curriculum (which is geared toward the high ability students) overly challenging and hence experience a negative impact on 1For models of academic standards as a requirement on the education outcome, see Costrell (1994, 1997); Betts (2008); Eisenkopf and Wohlschlegel (2012). 5 her learning outcomes. On the empirical side, there is a large existing literature estimating the impact of various vertical measures of the education technology, such as school quality and school resources (Card and Krueger,1992;Currie and Dee,1995,2000;Hanushek,1997,2006; Jacob and Lefgren,2004), class size (Angrist and Lavy,1999;Hoxby,2000;Krueger, 2003;Ding and Lehrer,2010;Chetty et al.,2011), teacher quality (Angrist and Lavy, 2001;Rivkin et al.,2005;Clotfelter et al.,2006;Aaronson et al.,2007;Rothstein,2010; Carrell and West,2010;Mueller,2013), and peer effects (Evans et al.,1992;Sacerdote, 2001;Zimmerman,2003;Angrist and Lang,2004;Arcidiacono and Nicholson,2005;Lyle, 2007;Carrell et al.,2008,2009). This literature tends to focus on the average treatment effect associated with the change in one of these vertical measures, since economic theory provides an unambiguous prediction as to the qualitative impact (the direction) of such a change on student learning outcomes. On the other hand, the focus is typically not on the distributional effect, since economic theory tends to be ambivalent as to how the quantitative impact of such a vertical change would vary across students. There is also a small but fast growing empirical literature that focuses on the distributional effect of matches between students and schools. For example, Light and Strayer (2000) examine whether the match between student ability and college quality affects the student’s college graduation rate. They find that while high-ability students are on average more likely to graduate from college than low-ability students, as expected, students of all ability levels are more likely to graduate if they attend colleges with quality level matching their ability level. In other words, high-ability students are more likely to graduate when attending high-quality rather than low-quality colleges, while the opposite is true for low-ability students. More recently, Arcidiacono et al. (2011) examine whether affirmative action leads to mismatch between lower-ability students and highly selective schools. They find evidence that, compared to the school, students are worse at predicting their post-enrollment achievement based on initial preparation. Thus, affirmative action can result in mismatches: had students known that they would perform worse than expected, they could have chosen a different (less selective) school. Similarly, Arcidiacono 6 et al. (2016) examine the difference in the graduation rates for minority science students across University of California campuses under affirmative action policies. They find that less-prepared minority students at higher-ranked campuses had lower persistence rates in science and took longer to graduate. Again, affirmative action can result in mismatches: had these minority students attended lower-ranked campuses and hence had they been better matched to universities according to their initial preparation, they would have reached higher graduation rates in STEM fields. This line of evidence – that lower-ability students enjoy better learning outcomes in less selective schools – hints at the existence of important factors that “horizontally” differentiate less selective schools from more selective schools. Our paper provides a theoretical explanation of the education curriculum as one possible horizontal factor. The paper that is most closely related to our paper is Duflo et al. (2011). In this study, they examine whether academic tracking helps or hurts low-ability students. Using randomized experimental data from Kenya, they find that tracking students by priorachievement raises scores for all students, even those assigned to lower achieving peers. To interpret these results, they argue that tracking allows teachers to better tailor their instruction level, and lower-achieving pupils are particularly likely to benefit from tracking when teachers have incentives to teach to the top of the distribution. Similar to our paper, their model allows both a “direct” peer effect (student-to-student spillovers) and an “indirect” peer effect, where the indirect effect arises when the composition of the class affects teacher effort as well as the target level of teacher instruction. Unlike our paper, their model does not allow the trade-off between the target level and the pace of learning, the two related parameters of the education curriculum in our model. Instead, they model the pace of learning as a result of teacher effort, which can be changed independently of the target level of instruction. In a sense, our paper can be viewed as moving along a given efficiency frontier of the education technology consisting of different curricula, while their paper can be viewed as improving the efficiency frontier when changes in the teaching environment (tracking) and stronger incentives (contract teachers) induce higher levels of teacher effort, which again is a vertical measure of the education technology. Alternatively 7 fixed effects γsand year fixed effects ηt. Finally, ist is the error term. Note that our focal interest is on the two variables qist and Ast, neither of which is directly measured. As will be discussed in the next section, the quasi-natural experiment of the G8 reform directly translates into an increase in Ast. Even if we do not have a quantitative measurement of the increase in the curriculum threshold, we can argue qualitatively that the G8 reform corresponds to an increase in the curriculum from one level (for all states under the old G9 regime) to another, higher, level (under the new G8 regime). In this sense, even though in theory the curriculum can take any value in the relevant range, for our empirical analysis we are only considering the difference between two particular curricula implemented in the G9 and G8 regimes. From here onward, we denote the curriculum associated with the old G9 regime as Aoand co, and the curriculum under the G8 reform as Anand cn, where Ao< Anand co< cn. On the other hand, when there is only limited information on student preparation qi, we use two different econometric approaches as described in detail below. 4.1 Difference-in-differences Suppose student initial preparations are not perfectly observed. As long as the distribution of qiremains stable before and after the curriculum change, we can treat it as an unobserved variable and integrate it out to estimate an average impact of the curriculum change. More specifically, consider two states sand rin two years tand w, such that Ast =Art =Arw =Aowhile Asw =An, namely state sstarted with the original G9 regime in year tbut implemented the G8 reform in year w, while state rmaintained the G9 regime in both years. Inserting these particular values of the applicable curricula into (5) and then taking the difference-in-differences, we have (hisw −hjst)−(hkrw −hlrt) = α((qi−qj)−(qk−ql))+((Aswqi−Astqj)−(Arwqk−Artql)) −(f(An)−f(Ao)) + δ((Xisw −Xjst)−(Xkrw −Xlrt)) + (isw −jst)−(krw −lrt)(6) 14 Even if we do not observe individual qdirectly, as long as the distribution of student preparation in a given state stays the same over time, we can integrate them out to get the expected value or the average level for the student population. Assumption 2 Let φst(·)be the distribution density function of student initial preparations for state sin year t, such that φst(·) = φs(·)with mean µs. Then, conditional on the observed variables X, the average reform effect can be expressed as follows: DiD(h) = µs(An−Ao)−(f(An)−f(Ao)).(7) Namely, after controlling for the impact of the observed variables on the test score, our DiD approach allows us to estimate the average reform impact on student test scores even when we do not observe student initial preparations. The validity of the DiD approach relies on the assumption of a stable distribution for a given state over the years. Similarly, we can break the overall average effect in (7) into two average effects, depending on whether a student’s preparation is above or below a given cutoff level, a crude binary measure of student preparation. If the cutoff level happens to be ˆq(as defined in Proposition 3), we have: DiD(h+) = Zq>ˆq φs(q)dq ×(An−Ao)−(f(An)−f(Ao)) >0, and DiD(h−) = Zq≤ˆq φs(q)dq ×(An−Ao)−(f(An)−f(Ao)) <0. Alternatively, for any given cutoff level q, even though the signs of DiD(h+)and DiD(h−) are not guaranteed to be positive and negative, we still expect the relationship DiD(h+)> DiD(h−), or equivalently, DiD(h+)−DiD(h−)>0. 15 Based on this, our DiD model is estimated by the following equations. For the overall average effect, we have: hist =β0+β1G8st +δXist +γs+ηt+ist,(8) where hist is the (standardized) PISA reading, mathematics, or science score measured in year tfor an academic-track student iin state s.G8st is the G8 reform indicator which equals one if a student observed in year tand in state sbelongs to the cohort treated by the G8 reform in that state, and zero otherwise. For the average effects within two subgroups of students, we have: hist =β0+β2G8st ×I(qist >ˆq) + β3G8st ×I(qist ≤ˆq) + δXist +γs+ηt+ist.(9) Our main interest is the relationship between β2and β3. Our theory predicts that β2> β3, which will be tested in the data. In contrast, β1is a weighted average of β2and β3, and is equivalent to the average reform effect across all students. 4.2 Quantile Regressions An alternative approach to deal with the unobserved qproblem is quantile regression, which allows us to examine potentially heterogeneous effects the reform has at different locations of the outcome distribution. More specifically, the conventional quantile regression approach relies on the common distribution assumption, that is, not only should the distribution of the unobserved variable qremains stable overtime, the distribution has to be the same across the treated and the control states. When this is the case, students at the τ-th quantile would have exactly the same preparation qτ, regardless of whether they are in a treated or control state, before or after the treatment. Thus, holding all other observed variables constant, test score difference at a given quantile τbetween the treated and the control state before and after the treatment can be attributed to the treatment itself, namely the G8 reform effect. We call this the quantile difference-in-difference 16 method (QDiD). To implement QDiD, we estimate the following quantile model: hτ,st =βτ,0+βτ,1G8st +δτXist +γτ,s +ητ,t,(10) where hτ,st is the test score at a given quantile τin state sand year t. Note also that all the parameters are quantile-specific. In particular, the quantile-specific βτ,1represents the treatment effect of the G8 reform at the particular quantile τ. However, the common distribution assumption is a well-known limitation of the quantile regression approach, which cannot be expected to hold in general. Without this assumption, the distribution of qcan be different in a treated state from that in a control state, and the test score difference at a given quantile may be attributed to either the preparation difference or the G8 reform itself, making the control state not a valid counterfactual for the treated state. To address this concern, we also use the Recentered Influence Function (RIF) method recently developed by Firpo et al. (2009), which explicitly relaxes the common distribution assumption.2More specifically, when the observed outcomes (in this case, test scores) vary monotonically with the unobserved variable (in this case, student preparation), RIF for the τth quantile as: RIF(Y;qτ) = qτ+τ− 1 {Y≤qτ} fY(qτ),(11) where 1 {Y≤τ}is an indicator variable that takes the value of 1 if Y≤qτand 0 otherwise, and fY(qτ)is the marginal distribution of Yaround the value of qτ. It has been shown that a RIF regression – defined for the τ-th quantile as E[RIF(Y;qτ)|X] = mτ(X)≈X0βτ– leads to a consistent estimate of the unconditional quantile treatment effect.3 For our analysis, instead of examining students at the same quantile across states and years (as in the QDiD case), the RIF method compares students with the same test score and hence located at potentially different quantiles of the distributions across states 2Given its flexibility, the RIF method has recently been applied to analyze a range of issues such as cigarette taxes (Maclean et al.,2014) and child care (Havnes and Mogstad,2015). 3See Firpo et al. (2009); Borah and Basu (2013). 17 and years. More specifically, consider a year before the reform, let us call it year t. For a given test score h, we can determine the corresponding quantiles τst in state sand τrt in state r. Next, moving on to a subsequent year wwhere state shas implemented the reform but not state r. Again, for the same test score h, we can determine the corresponding quantiles τsw and τrw respectively. The impact of the G8 reform, measured as the change in the population shares that remain below the given test score h, is then given by −((τsw −τst)−(τrw −τrt)). This probability difference is then divided by a kernel estimate of the joint density of test scores at the level hto arrive at the associated treatment effect. We call this the RIF-DiD method.4For the RIF-DiD method to work, the distribution of the unobserved variable (student preparation) can be different across treated and control states, as long as it remains stable over time within each state. This is much less restrictive compared to the common distribution assumption required for the QDiD method. Besides the difference in the underlying distribution, there is also a difference in terms of interpretation of the estimation results. More specifically, the QDiD estimates can be viewed as the conditional quantile treatment effect, where heterogeneity in the observed variables implies potentially many different distributions. This matches closely with our theoretical model interpretation of the treatment effect due to a curriculum change, holding everything else constant. However, the conditional quantile treatment effect can be quite sensitive to the variables that it conditions on (Borah and Basu,2013;Maclean et al.,2014). On the other hand, the RIF-DiD estimates can be viewed as the unconditional quantile treatment effect, where the many different conditional distributions are aggregated into one common unconditional distribution, given the realized values of the observed variables in the data. As a result, the unconditional quantile treatment effect is easily interpreted as that applicable to the entire student distribution. However, its link to our theoretical prediction of the curriculum effect is less direct. For example, suppose in the data, well-prepared students in treated states concentrate more heavily in middle 4We implement the RIF-DiD estimation procedure using the STATA ado file rifreg – downloaded from http://faculty.arts.ubc.ca/nfortin/datahead.html (last accessed December, 2015). The RIF is computed using a Gaussian kernel with an optimal bandwidth. 18 quantiles instead of top quantiles of the unconditional test score distribution, possibly due to individual heterogeneity in observed variables such as family background. In this case, the QDiD method can still accurately estimate the effect of a curriculum change, controlling for the differences in observed variables. On the other hand, the RIF-DiD method will conclude that the reform has a stronger effect in middle quantiles than top quantiles, because it reflects both within-group difference (that is, groups of the same family background) and between-group difference (groups of different family background). A further limitation of both the QDiD and the RIF-DiD method is that, despite the importance of clustering standard errors at the treatment (state) level to avoid overstating precision (Bertrand et al.,2004) is widely recognized, a statistically valid method to cluster standard errors has not been developed yet. This is further complicated by the sampling weights associated with the observations in the complex survey design. As a result, we can only report the standard error for QDiD assuming i.i.d. residues, while that for RIF-DiD is bootstrapped using 200 repetitions. 5 Data 5.1 The policy variable - G8 reform Educational policy in the Federal Republic of Germany is under the responsibility of the sixteen federal states. Children typically enroll in primary school at the age of six, and continue on to secondary school after four years. At the beginning of grade 5, students are tracked into three types of school: The basic-track school (Hauptschule) and the middletrack school (Realschule) provide vocational oriented schooling through grade 9 or 10; the academic-track high school (Gymnasium) leads to university entrance qualification called “Abitur”. Beginning in 2001, most German states introduced the so called G8 reform. The length of the academic-track curriculum was shortened by one year (from 9 to 8), but the total amount of curricular content to be covered as a graduation requirement was held fixed. As a consequence, the G8 curriculum has a faster progress rate – and, implicitly, 19 a higher curricular threshold – than the G9 curriculum. Using the terminology of our theoretical model, the G8 regime adopted a more challenging curriculum. Figure 1offers a visual summary of the G8 reform implementation over time and across states. We refer to Andrietti (2015,2016) for a detailed discussion of the G8 reform implementation and for a definition of the G8 policy variable. For our analysis, the G8 reform can be viewed as a quasi-natural experiment: namely it was mostly driven by considerations of the labor market conditions and demographic changes. For example, in earlier policy discussions, then-federal secretary of education Jürgen Mölleman called on stakeholders to engage in deliberations on the subject “Twel- ve years (including primary school) to the Abitur.” In his opinion, Gymnasium grades should be reduced from 9 to 8 years for the following reasons: “[German] graduates are two to three years older than their peers against whom they compete for jobs in the European labor market. ... German pension systems and demographics (characterized by a significant fraction of senior, retired citizens) cannot support such a late start of employment by young adults. ... Students reach the age of majority at 18 and should have completed post-secondary schooling by then, especially since the motivation for studying decreases with age. At age 25, they should have completed college, including military or civil service, and should have reached full social and economic independence. ... In addition, many schools do not fully utilize the 13th school year. Therefore, a decrease in education quality [associated with reform] can be avoided through more intensive instruction in smaller classes and, possibly, all-day instruction programs. (Translation by author)” (Wiater,1996). Similarly, when the reform was actually implemented, its was implemented for similar reasons: “Following a change of government, Saarland was the first West German state to reduce the number of grades taken to reach Abitur from 13 to 12, effective academic year 2001/02. Driving this change was the supposed disadvantage of Saarland’s graduates when entering the labor market caused by Germany’s comparatively long schooling duration. ... As mentioned earlier, reducing the number of years of education is one of several measures aimed at lowering the age at which academically qualified workers enter the labor force, which is regarded as too high when 20 compared internationally and, in light of the rising demand for highly educated workers in a globalizing world, is expected to result in a competitive disadvantage for German university graduates, and hence for Germany itself. ... In order to protect social insurance systems, the palpable aging of the population, coupled with the simultaneous decline in births and population, necessitates an earlier entry of young adults into a longer phase of gainful employment. (Translation by author)” See Kühn et al. (2013) for more detailed discussions. From a student perspective, the curriculum change is exogenous, and DiD is a suitable method to estimate the average treatment effects among subgroups of students. In a sense, the G8 reform is a policy-induced instrument for the actual curricula implemented at different schools across different years. Furthermore, since the G8 reform happened at the state level, the stability of their underlying preparation distribution is more likely to hold than that at more disaggregate levels, as there is very limited student mobility across state borders. Finally, Andrietti (2015) provides further support to the quasiexperimental nature of the G8 reform, documenting that high school enrollment patterns did not change in response to the introduction of its more challenging curriculum. 5.2 PISA data The empirical analysis is based on a dataset that pools the first five waves of PISA assessment (2000, 2003, 2006, 2009, and 2012) for Germany.5While PISA is conducted by the OECD in a number of countries sampling 15-year-old students, independent of grade, national grade- and/or age-based extensions of the study were conducted in Germany for all PISA cycles, with the purpose of providing a sample large enough to allow comparisons between the different federal states. Given that the age-based PISA 2009 sample has not been released with state identifiers, our empirical analysis is based on grade-9 samples. In particular, our samples include all ninth-graders enrolled in academic-track high schools, with a valid test score assessment and with non-missing values on grade repetition.6 5Baumert et al. (2009); Prenzel et al. (2007,2010); Klieme et al. (2013); Prenzel et al. (2015) 6Rather than dropping a small number of observations where information is missing on other background variables, we recode missing values to zero, and define missing values indicators for the variables included in a specification. In results available upon request, we find, however, that our main results are 21 It is worth pointing out that a sample of ninth-graders, like the one we use, includes high school grade repeaters. The latter spend one extra year in high school, compared to everyone else. The grade repetition essentially slows down the progress rate for these students, i.e., they learn the same amount of academic content with extra time and more slowly than dictated by the G8 reform. The extra year of schooling or remedial work adds up to what they would otherwise have achieved in the same amount of time as everyone else. Thus, grade repetition leads to potential upward bias in the reform effect for the grade repeaters. Despite the potential upward bias, if we still find evidence that grade repeaters benefit less from the G8 reform compared to the non-repeaters, we will know that the performance gap between the two subgroups of students will be even bigger when the upward bias is properly accounted for. In other words, our estimate offers a lower bound of the true effect. PISA tests cover three different subjects (reading, mathematics, and science), assessing a range of relevant skills and competencies. Each subject is tested using a broad sample of tasks with differing levels of difficulty to represent a coherent and comprehensi- ve indicator of the continuum of students’ abilities.7An issue related to the pooled nature of our data is the comparability of subject-specific student assessments across PISA cycles. While reading assessments are comparable across all cycles, mathematics and science assessments underwent major revisions in 2003 and 2006 respectively, the first time they were considered the main subject. As a robustness check, we use both the full sample (all five waves) and the truncated sample (excluding 2000 for mathematics, excluding 2000 and 2003 for science) for estimation. 5.3 Control variables Two groups of variables, defined at the student- and school-level, are employed as controls in the empirical analysis. Descriptive statistics on these variables are reported in Table robust to the exclusions of missing values observations. 7Using item response theory, PISA maps student performance in each subject on a scale with an international mean of 500 and a standard deviation of 100 across the OECD countries included in the study. The scores are averages of plausible values, which are drawn from a distribution of values that a student with the given amount of correct answers could achieve as a test score (OECD,2012). 22 1. Student controls include a set of demographic and socio-economic characteristics, as well as a grade retention dummy that controls for different schooling experiences. The demographic characteristics include a dummy indicating female students and a quadratic age term (in months) that controls for potential age/maturation effects. The socioeconomic characteristics include an indicator for the number of books at home, two indicators for parents’ highest educational level (ISCED), as well as the Highest International Socio-Economic Index (HISEI), which uses the higher of the two parents’ ISEI scores or the only available parent’s ISEI score. There are also variables indicating a student’s migration background, namely whether the student was born in a foreign country, whether a foreign language is spoken at home, and whether at least one of the parents was born in a foreign country. School controls include the total number of enrolled students, the percentage of girls enrolled, the student-teacher ratio, as well as dummy variables indicating urban schools and privately run schools. Moreover, although PISA does not provide objective measures of the school financial situation, school resources are proxied by the school principals’ subjective assessments of whether a lack of instructional material or a lack of computers hindered instruction at their school. 6 Results 6.1 DiD results The results obtained estimating different specifications of equations (8) and (9) on different samples are reported in Tables 2to 4. Within each table, the results are organized in panels, where the dependent variables are standardized test scores in reading, mathematics, and science, respectively.8Standard errors are clustered on the state level to account 8Estimation is performed according to the procedure recommended in OECD (2012). For each domain, OLS regressions are run separately on each of the five plausible values, and the results aggregated to obtain the final estimated coefficients and their respective standard errors. 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Summary statistics Variable Mean SD PISA scores Reading 573.19 55.17 Mathematics 579.66 58.14 Science 588.08 60.89 Student controls: Female 0.54 0.50 Age (in months) 185.19 5.47 High school grade repeated 0.08 0.26 Parents’ ISCED 3-4 0.29 0.46 Parents’ ISCED 5-6 0.63 0.48 Parents’ ISEI 58.63 16.54 Books in house: >100 0.60 0.49 Only child 0.31 0.46 Kid born in foreign country 0.04 0.20 Parents born in foreign country 0.13 0.34 No German spoken at home 0.04 0.20 School controls: School enrollment 799.08 350.33 % of girls enrolled 49.57 14.89 Student-teacher ratio 14.66 5.88 Lack of computers 0.34 0.47 Lack of textbooks 0.23 0.42 Urban school 0.26 0.44 Private school 0.07 0.26 Policy variables: G8 reform 0.41 0.49 Observations 31,383 Notes: The sample includes academic-track ninth-graders from PISA 2000-2012 pooled data with a valid assessment in reading and nonmissing values on grade retention. 37 Table 2. DiD regressions: main samples Baseline Main (1) (2) (3) (4) (5) (6) Panel A: Reading G8 0.073** 0.098** 0.072** 0.083** (0.021) (0.018) (0.022) (0.020) G8 ×high school grade not repeated 0.098** 0.083** (0.018) (0.020) G8 ×high school grade repeated -0.256** -0.354** -0.078* -0.161** (0.037) (0.033) (0.041) (0.035) Adjusted R20.028 0.034 0.034 0.104 0.105 0.105 Observations 31,383 Panel B: Math G8 0.069* 0.091** 0.061* 0.072** (0.040) (0.038) (0.033) (0.032) G8 ×high school grade not repeated 0.091** 0.072** (0.038) (0.032) G8 ×high school grade repeated -0.217** -0.307** -0.079* -0.150** (0.045) (0.029) (0.041) (0.030) Adjusted R20.031 0.036 0.036 0.138 0.139 0.139 Observations 27,381 Panel C: Science G8 0.085** 0.109** 0.080** 0.093** (0.022) (0.022) (0.019) (0.019) G8 ×high school grade not repeated 0.109** 0.093** (0.022) (0.019) G8 ×high school grade repeated -0.225** -0.334** -0.098** -0.190** (0.039) (0.038) (0.036) (0.032) Adjusted R20.028 0.033 0.033 0.114 0.116 0.116 Observations 27,661 State fixed effects X X X X X X Cohort fixed effects X X X X X X Student controls X X X School controls X X X Notes: Specifications (1)-(3) are baseline specifications. Specifications (4)-(6) are main specifications, including student and school controls. The main specifications do not include high school grade retention among the controls. Final student weights are used in all regressions. Standard errors clustered on state are reported in parentheses. ∗∗ and ∗indicate significance at 5 and 10 percent levels, respectively. The samples in panel A, B, and C include academic-track ninth-graders from the pooled PISA 2000-2012 dataset with a valid assessment in either reading, math, or science, respectively, and with non-missing values on grade retention. 38 Table 3. DiD regressions: truncated samples Baseline Main (1) (2) (3) (4) (5) (6) Panel B: Math G8 0.081** 0.103** 0.077** 0.087** (0.040) (0.039) (0.033) (0.033) G8 ×high school grade not repeated 0.103** 0.087** (0.039) (0.033) G8 ×high school grade repeated -0.204** -0.306** -0.059 -0.145** (0.044) (0.029) (0.041) (0.031) Adjusted R20.033 0.038 0.038 0.140 0.141 0.141 Observations 23,036 Panel C: Science G8 0.095** 0.119** 0.103** 0.116** (0.025) (0.028) (0.031) (0.033) G8 ×high school grade not repeated 0.119** 0.116** (0.028) (0.033) G8 ×high school grade repeated -0.215** -0.334** -0.064 -0.179** (0.040) (0.040) (0.045) (0.041) Adjusted R20.028 0.036 0.036 0.130 0.131 0.131 Observations 15,736 State fixed effects X X X X X X Cohort fixed effects X X X X X X Student controls X X X School controls X X X Notes: Specifications (1)-(3) are baseline specifications. Specifications (4)-(6) are main specifications, including student and school controls. The main specifications do not include high school grade retention among the controls. Final student weights are used in all regressions. Standard errors clustered on state are reported in parentheses. ∗∗ and ∗indicate significance at 5 and 10 percent levels, respectively. The sample in panel B (C) includes academic-track ninth-graders from PISA 2003-2012 (2006-2012) with a valid assessment in math (science) and non-missing values on grade retention. 39