THE RESPONSES OF YOUTH TO A CASH TRANSFER ...faculty.smu.edu/millimet/classes/eco7377/papers/humlum...intra-household transfers mitigates the observed effects of the transfer. Nonetheless,

THE RESPONSES OF YOUTH TO A CASH TRANSFERCONDITIONAL ON SCHOOLING: A QUASI-EXPERIMENTAL

STUDY

MARIA KNOTH HUMLUM AND RUNE MAJLUND VEJLIN*

School of Economics and Management, Aarhus University, Denmark

SUMMARYWe estimate the effect of cash transfers given to youth conditional on high school attendance on the labor supplydecisions and academic performance of youth. We exploit differences in the size of the total transfer receivedbased on timing of birth to identify the causal effects of interest. Specifically, individuals born late in a quarterreceive a larger total transfer than comparable individuals born early in the following quarter. We find that thetransfer increases the labor market participation of youth and the number of months worked. The estimated effectis larger for individuals from low-income families. The results suggest that some youths are borrowingconstrained. Since we find no evidence of corresponding effects on academic performance, alleviating the con-straint appears only to affect consumption decisions and not human capital investment. Copyright © 2011 JohnWiley & Sons, Ltd.

1. INTRODUCTION

The provision of cash transfers to parents, children and youth is an integral part of public policy inmany Organisation for Economic Co-operation and Development (OECD) countries. However, it isan open question whether cash transfers given to families is an effective way of increasing equalityof opportunity, as is the goal. In this paper, we investigate the relationship between adolescentoutcomes and a publicly provided cash transfer to youth given conditional on high school attendance.Our contribution is twofold. First, we provide evidence on the effect of giving cash transfers to youth ina setting characterized by a high general transfer level and free access to education. Second, using largeadministrative datasets covering the entire Danish population combined with a quasi-experimentalsetup, we are able to identify the causal relation between cash transfers and adolescent behavior andoutcomes.Although the specific elements of the family benefit scheme, including the degree of means testing,

the generosity of the benefit, and the ages of the child at which a family is eligible, vary widely acrosscountries, many of the schemes share a common setup. Figure 1 shows the eligibility of parents forbenefits by age of child in selected OECD countries. Unconditional transfers for families until the childis around 15–20 years old are common.1 For families with older children, many countries, e.g.Germany and Australia, continue the provision of family benefits, but the transfer is then often condi-tional on the child’s school attendance. Interestingly, some of the countries typically considered rela-tively generous in terms of public transfers, such as Denmark, the Netherlands, and Norway, appearto have little support for families after the child’s 18th birthday. The explanation is that transfers for

* Correspondence to: Rune Vejlin, School of Economics and Management, Building 1322, University of Aarhus, Aarhus 8000Denmark.E-mail: [email protected]

1 Here ‘unconditional transfer’ is understood to be a transfer that is unconditional on the behavior of the family, but not neces-sarily unrelated to the characteristics of the family, e.g. family income.

Copyright © 2011 John Wiley & Sons, Ltd.

JOURNAL OF APPLIED ECONOMETRICSJ. Appl. Econ. (2011)Published online in Wiley Online Library(wileyonlinelibrary.com) DOI: 10.1002/jae.1267

families with adolescent children in these countries (and others) are given to the child—not theparents.2

The primary goal of most family benefit programs is to promote equality of opportunity. In otherwords, the goal is to ensure that children from disadvantaged families have the same opportunitiesin life as other children. At least part of the intergenerational correlation in income and education,for example, is generally considered to be evidence that children do not have equal life chances. Recentevidence put forward by Belley and Lochner (2007) suggests that there remains scope for policies pro-moting equality of opportunity. Using the National Longitudinal Survey of Youth (NLSY79 andNLSY97), they show that family income is still an important determinant of the educational attainmentof youth in the USA.

Providing families with family benefits allows parents—or adolescents in our case—to increasehousehold consumption and investment. From a theoretical perspective, transfers could potentiallycause adolescents to invest more in their human capital accumulation, but may also simply increaseconsumption with no long-term effects on academic performance. If credit markets worked perfectly,we could expect only very limited effects from increasing the size of the transfer, since the transferconstitutes a minor part of lifetime income. In the presence of borrowing constraints, however, increas-ing the size of the transfer may have more substantial effects. A priori, we would expect adolescents towork less if given a higher transfer, but the corresponding effects on human capital accumulation areless clear. If there is a strong complementarity between leisure time and consumption, then increasingthe transfer might even cause adolescents to spend less effective time studying.

While a number of studies investigate the effects of family income or cash transfers to families onchild and family outcomes, these studies tend to focus on low-income families in developed countries;see, for example, Dahl and Lochner (2008), who use changes in the Earned Income Tax Credit asexogenous variation, or families in developing countries, e.g. Attanasio et al. (2010a) for Colombiaand Attanasio, Meghir and Santiago (2010b) for Mexico. In addition, the existing literature focusesprimarily on families with young children, but there is little evidence concerning generous transferprograms for families with adolescent children. The lack of evidence is striking when one takes intoaccount the extent of public transfers to these families (see Figure 1 and the discussion above). Recent

2 This type of transfer is typically conditional on schooling and is often named accordingly, e.g. student financial aid or educa-tion maintenance allowance. The fact that these transfers are often means tested against parental income emphasizes that thesetransfers are closely related to family benefits received by parents of adolescents in other countries.

10

12

14

16

18

20

22

24

26

28

30

Age

of c

hild

AUSAUT

BELCAN

CZEDNK

FINFRA

DEUGRC

HUN ISL

IRL

ITA

LUX

NLD NZLNOR

POLPRT

SVKESP

SWE

UKM

Source: OECD (2007)

Eligibility of parents for unconditional transfers

Eligibility of parents for transfers conditional on schooling

Figure 1. Eligibility of parents for family cash benefits (including non-wastable tax credits) for selected OECDcountries by age of child

M. K. HUMLUM AND R. M. VEJLIN

Copyright © 2011 John Wiley & Sons, Ltd. J. Appl. Econ. (2011)DOI: 10.1002/jae

exceptions include Dearden et al. (2009) and Sabates and Feinstein (2008), who use the pilot programfor the Education Maintenance Allowance in the UK to investigate the effects of conditional cashtransfers to youth on dropout rates and crime, respectively. Although existing studies on conditionalcash transfers for youth find relatively large effects, this may not translate into a setting such as theone in Denmark, where generous transfers are already in place. Dynarski (2004) provides an examplewhere the introduction of a performance-based universal aid program for college students in Georgiaincreased the college enrollment rate very little or not at all. Thus the universal transfer does not induceindividuals to enroll in college but rather operates simply as a transfer to those who would have chosento attend college anyway.The cash transfer analyzed in this paper is a combination of a universal and a means-tested transfer.

In order to identify the causal effect of the transfer on adolescent outcomes, we employ a convenientfeature of the payout scheme that results in a discontinuity in the amount of total transfers receivedby date of birth. Like many studies in the education literature attempting to identify causal effects,we use a regression discontinuity design (Angrist and Lavy, 1999; van der Klaauw, 2002). This ismade possible by rich administrative datasets from Statistics Denmark containing the exact date ofbirth. We argue that this provides us with an appealing application of the regression discontinuitydesign, and specifically an application where many of the problems that often arise when using dateof birth as an instrument (see, for example, Bound and Jaeger, 1996; Buckles and Hungerman, 2008)are not likely to be present.Our analyses focus on in-school outcomes, i.e. employment during high school and academic

outcomes such as high school grade point average (GPA). In order for this approach to be valid,expectations regarding the amount of financial aid received cannot affect decisions regarding highschool enrollment and dropout. However, given that Dearden et al. (2009) find the effects of a cashtransfer on the participation rates of 16- to 18-year-olds to be substantial, this is not obviously true.We argue that this margin is less likely to be affected in our setting and verify this empirically. We findthat an increase in the size of the cash transfer of about USD 560 on average decreases labor marketparticipation by about two percentage points. Ruhm (1997) argues that high school employment to alarge extent is an investment that yields a future payoff on the labor market. Our results suggest thathigh school employment is at least to some extent consumption motivated. When youths receive ahigher income, they substitute away from labor market work. If high school employment is purelyan investment, we expect little effect from a change in transfers on work behavior. Policymakers hopethat cash transfers decrease the amount of time that adolescents spend working such that more time isavailable for school work. We find a very small and statistically insignificant effect on high schoolGPA of increasing the transfer. High precision allows us to rule out any substantial adverse effectson GPA of a comparable lowering of the transfer. However, we cannot rule out that the presence ofintra-household transfers mitigates the observed effects of the transfer. Nonetheless, for policy guid-ance, the estimated parameter is the parameter of interest as it captures the total effect on students’behavior. At current levels, at least, the cash transfer to high school students is neutral with respectto educational outcomes and educational choices, suggesting that this large-scale transfer programsimply allows recipient households to increase consumption of other goods.Finally, we investigate whether the results differ across characteristics of youth and their families. In

the presence of borrowing constraints, one would expect youth from disadvantaged families to be moreresponsive to a change in the transfers. What we observe is indeed that individuals from low-incomefamilies react more strongly in terms of labor market behavior, although the differences tend to be onlymarginally significant. With respect to GPA, the estimated effects of the transfer vary remarkably littleacross subgroups.The structure of this paper is as follows. Section 2 describes the publicly provided cash transfers for

high school students in more detail, along with the specific features of the system that our identificationstrategy relies on. Next, Section 3 explains the empirical approach, while Section 4 outlines the data,

RESPONSES OF YOUTH TO A CASH TRANSFER


and Section 5 presents a graphical analysis of the regression discontinuity and the estimation results,along with some of the robustness checks used to validate our results. Section 6 concludes.

2. CASH TRANSFERS FOR HIGH SCHOOL STUDENTS IN DENMARK

High school students in Denmark receive a monthly cash transfer from the State Education Fund afterthey turn 18. The description below covers what the transfer system was like from 1996 to 2004, whichis the period we focus on in the empirical analysis. Emphasis is placed on elements relevant to the iden-tification strategy. In Denmark there are two major branches of upper secondary education: vocationaland high school.3 The focus of this paper is on high school education, although the transfer system isessentially the same for vocational education.4

The main purpose of the cash transfers is to promote equality of opportunity. The aim of the transfers isto ensure that the educational decisions of adolescents are not affected by their family income. The transferconsists of two elements: a basic, universal transfer and a means-tested supplement. In order to limit theamount of work outside of school, a student is obligated to pay back the transfers if the amount of workexceeds a certain threshold.5 The size of a basic monthly transfer in 2000 was DKK 1252, whichcorresponds to about USD 155. A means-tested supplement is given to individuals with adjusted parentalincome below a certain threshold.6 Individuals not living with their parents received a higher basic rate.

7

2.1. Eligibility and Payout

Individuals become eligible for the transfer in the quarter following the quarter in which they turn 18.The monthly transfer is paid out in advance; i.e. the transfer for April is paid out on the last bankingday of March. In practice, this implies that individuals born on 31 March in a given year will receivetransfers in April, May, June, July, etc. the year they turn 18, while individuals born just one day later,on 1 April, in the same year do not begin to receive transfers until July. Thus individuals born late in aquarter receive a higher total transfer during high school than individuals born early in the followingquarter.8 Apart from the cash transfers, the income of high school students is likely to stem fromtwo main sources, namely parental transfers and labor market work. The monetary gain incurred frombeing born late in a quarter relative to early in the following quarter is USD 465 (3�USD 155) for ahypothetical student receiving only the basic transfer and higher for students receiving the means-tested supplement.

3 Vocational education covers training for specific trades such as being a craftsman, automobile mechanic or hairdresser. Theterm ‘high school education’ encompasses all of the standard high school educations. Upper secondary education encompassesboth of these terms.4 It is convenient to restrict attention to high school students in order to obtain comparable outcome measures. The effects of cashtransfers on the work behavior and educational choices of youths in vocational educations are definitely of interest, but they arebeyond the scope of this paper.5 The limits are the same for high school students and students in higher education. In 2000, the thresholdwas approximatelyDKK 5049 (about USD 625) in months where the student received a transfer and DKK 12,609 (about USD 1560) in monthswhere no transfer was received. The thresholds are so high that the number of high school students affected is relatively small.6 In 2000, the threshold was DKK 378,974, corresponding to an annual income of about USD 47,000. For individuals with ad-justed parental income below the threshold, the supplement roughly decreases linearly with parental income. The maximum sup-plement, DKK 1973, was given to individuals with adjusted parental income below DKK 216,876. Parental income is adjustedfor the number of children in the household; i.e. there is a deduction for additional children in the household. Parental incomeonly includes the income of parents who are part of the child’s household.7 To receive the higher basic rate, DKK 2504 in 2000, individuals had to meet at least one of the following criteria: (i) the dis-tance between the family home and the school had to be 20 km or more; (ii) the transportation time (using public transportation)from the family home to the school had to be more than 75 minutes; (iii) the students had to have been living on their own con-tinuously for at least 12months before becoming eligible for the transfer; or (iv) the presence of exceptional circumstances in thefamily home.8 Monthly transfers cease the month after high school graduation.



2.2. Related Public Transfers

Danish parents begin receiving quarterly child benefit in the quarter following the quarter in which thechild was born and continue receiving it until the quarter the child turns 18. The size of the benefitvaries according to the age of the child. For our sample, the quarterly benefit received for a 17-year-old child was DKK 2100 in 2000 (about USD 260). Obviously, this implies an additional differencebetween individuals born late and early in a quarter. For example, the parents of a child born 31 Marchwill receive child benefits in the first quarter in the year the child turns 18, but the parents of a childborn 1 April will receive child benefits in both the first and the second quarter. The empirical strategyoutlined in the next section takes advantage of the discontinuity in the size of the total transfer duringhigh school by date of birth. Since there is a similar discontinuity in the size of the child benefitreceived by the parents, we will only be able to identify a combined effect of shifting transfers fromparents to children (about USD 260) and of increasing the size of the transfer (about USD 205 for ahypothetical student receiving only the basic transfer).

3. EMPIRICAL APPROACH

There are several methods that can be used to identify the effects of interest in our case, but becausethere is a discontinuity in the total transfer received by date of birth a regression discontinuity (RD)approach is particularly well suited for our estimation problem.

3.1. Applying the Regression Discontinuity Design

The basic idea behind our identification strategy is simple, namely that individuals born around thesame time are on average similar. However, due to specific rules regarding payout of transfers, youngindividuals attending high school receive differential transfers by date of birth. Individuals born late ina quarter receive a higher total transfer than comparable individuals born early in the following quarter,but it is plausibly random whether a given individual is born late in a quarter or early in the followingquarter. For each season and year of birth combination, there is a separate discontinuity and ourestimation strategy will take this into account. We will use the term ‘season of birth’ to reflect being bornin one of the following four periods: December–January, March–April, June–July, and September–October. For expositional purposes, we restrict attention to the setup with one season and year of birthcombination for now.Let Di be an indicator for whether or not individual i is born late in a quarter. Let xi be a count var-

iable that counts the distance in days from the first day of a quarter (x0) to the date of birth.9 Formally:

Di ¼ 1 xi < x0½ � (1)

Based on their date of birth, individuals are allocated to the treatment group (born late in a quarter)or control group (born early in a quarter).The RD setup requires that the total size of the transfer received jumps discontinuously at x0, and,

additionally, that the outcome of interest would be a smooth function of date of birth around the dis-continuity point if there were no discontinuity in the size of the transfers. In other words, if allindividuals receive the same amount of transfers, individuals born late in a quarter are similar toindividuals born early in the following quarter. Obviously, if this were not the case, a discontinuityin academic performance, for example, could not credibly be attributed solely to the discontinuity in

9 The discontinuity point is assumed to be x0 = 0, and xi is less than zero for individuals born late in a quarter and greater than orequal to zero for individuals born early in a quarter—e.g. xi= 0 for an individual born 1 April.



the size of the transfer. However, this assumption does not imply that identification relies on smooth-ness in the outcome variables in calendar time. One example is labor market outcomes. If firms tend tohire workers around the beginning of a month, labor market supply may jump discontinuously as afunction of calendar time. However, as long as this practice does not vary by date of birth and careis taken with respect to construction of outcome measures, this does not violate the smoothnessassumption.

Several studies have used date of birth as a source of exogenous variation in a variable of interest (e.g.Angrist and Krueger, 1991, for educational attainment).10 This has been criticized on the grounds thatthere are systematic differences in parental characteristics and child outcomes across season of birth (e.g.Bound and Jaeger, 1996; Buckles and Hungerman, 2008). The strategy we propose is not susceptibleto this criticism since it entails comparison of individuals born within the same season.

A potential pitfall of our strategy, however, is that youths may be forward looking. The differencesin transfers received by date of birth may affect educational choices prior to eligibility for the transfer.In other words, individuals in the treatment group have an increased incentive to enroll in high school.The issue is addressed in Section 5 and we find that it does not invalidate our results.

3.2. Econometric Models

To highlight some of the important issues of our estimation strategy, we begin by considering the para-metric estimation model. Subsequently, we will discuss nonparametric estimation, which is our pre-ferred estimation method.

Let yi be the outcome of interest for individual i, e.g. academic performance. Consider the followingparametric regression model for a single season and year of birth combination:

yi ¼ aþ b�Di þ g xið Þ þ dd18i þ g�Zi þ ei (2)

where xi and Di are defined above. The parameter b captures the causal effect of the differences intransfers across the treatment and control groups. The effect of distance from x0 to date of birth onthe outcome, g(xi), is modeled as a linear function. Date of birth is not expected to have substantialeffects on academic performance or labor market outcomes in the short time spans we consider. Fora single season and year of birth combination, xi captures not only distance from x0 but also age atthe time of measurement of outcomes measured at the same point in calendar time. For outcomes thatare potentially measured at different points in calendar time, xi and an indicator variable for turning 18in the first year of high school, d18i, capture age at the time of measurement. Zi is a vector of back-ground characteristics, such as gender, high school characteristics, and parental characteristics. ei isthe error term.

Let bts be the treatment effect for individuals born in season s of year t. We obtain estimates of theseason and year-of-birth specific treatment effects from estimation of a model similar to (2), where theintercept, the treatment effect and the effect of xi on the outcome are allowed to vary across season andyear of birth. The model is estimated by ordinary least squares. The estimate of the total treatmenteffect, b^P , is the weighted average of the estimated season and year-of-birth specific treatment effects:

b̂P ¼ ΣtΣsntsb̂ts

ΣtΣsnts(3)

where nts is the number of individuals in the sample born in season s of year t.

10 For more examples of studies using date of birth as a source of exogenous variation, see Buckles and Hungerman(2008).



Estimation using the parametric model described above requires potentially restrictive assumptionson the relationship between the outcome of interest and xi. We therefore turn to nonparametric estima-tion methods. As shown by Hahn et al. (2001), the treatment effect in an RD design is nonparamet-rically identified under relatively weak assumptions.

11

Let us again focus the discussion on a single season and year of birth combination. In the case wherethe treatment effect, b, is constant across individuals, the only assumption needed for nonparametricidentification is that of smoothness in the outcome in the absence of treatment described earlier. Forheterogeneous treatment effects, only E[bi|xi= x0] can be nonparametrically identified. In the limit, thenonparametric estimator divided by the average difference in transfers at the discontinuity point willbe equivalent to an IV Wald estimator obtained from a regression of academic performance, for exam-ple, on the amount of transfers received using Di as an instrument for transfers (see Hahn et al., 2001).The nonparametric estimator employed is the local linear regression (LLR) estimator, which has

better boundary properties and a smaller bias than a standard kernel-based estimator (see Hahnet al., 2001). A triangle kernel is used for weighting as it is boundary optimal, which is convenientin the RD application (see Cheng et al., 1997). We will discuss the choice of bandwidth in Section5.5. Again, the estimate of the total treatment effect is the weighted average of the estimated seasonand year-of-birth specific treatment effects.

3.3. Interpretation of the Treatment Effect

The estimated causal effect is interpreted as an average treatment effect (ATE) at the discontinuitypoint.12 In our application, it seems reasonable to assume that we can extrapolate to individuals bornrelatively far away from the discontinuity point. The estimated causal effect is an average effect ofincreasing the transfer by a certain amount on average. Since part of the transfer is means tested,individuals are in fact receiving non-homogeneous treatments. Therefore, the ATE is an aggregationof the effects of these different treatments on the individuals in the population.The interpretation of the treatment effect depends on the assumptions made concerning intra- house-

hold transfers that are unobservable to us, i.e. transfers from parents to children. Consider the case of ahypothetical youth receiving only the basic transfer. If we assume that the size of parental transfers isthe same for the treatment and control groups, the estimated parameter is the ATE of increasing thetransfer to the student by USD 465 and decreasing the transfer to parents by USD 260. On the otherhand, if we assume that the size of parental transfers varies across the treatment and control groups, theestimated parameter is the ATE of increasing the transfer to the student by USD 465 and decreasing thetransfer to parents by USD 260 and changing the intra-household transfer by some unobservable amount.If parental transfers differ across the treatment and control groups, we expect the control group to

receive the higher parental transfer. In this case, the estimated treatment effect will be biased towardszero compared to a parameter measuring the effect of an increase in public transfers to students holdingparental transfers constant.13 The estimated parameter is policy relevant as it measures the effect ofchanging the transfer on student behavior.

11 According to Lee and Card (2008), the estimate of the treatment effect is not nonparametrically identified for a discrete treat-ment assignment variable. We measure xi —the distance from date of birth to the beginning of a quarter—in days. We find that avariable measured in days is sufficiently close to being continuous and we proceed under this assumption.12 In principle, the estimated parameter is an intention-to-treat effect, but since the take-up rate is likely to be close to 100% weinterpret the estimates as average treatment effects. Based on our data, the relevant take-up rate is estimated to be at least 98%.13 The lack of inclusion of intra-household transfers is a shortcoming inherently present in observational studies. Intra-householdtransfers are potentially affected by the treatment and, even if observed, inclusion of this variable could therefore introduce bias inthe treatment effect (Rosenbaum, 1984). Anecdotal evidence suggests that the mean size of parental transfers to children aged 17in Denmark is about USD 50 per month (Erichsen, 2009), implying that differences in intra-household transfers across the treat-ment and control groups would be relatively small compared to the differences in public transfers.



4. THE DATA

We employ administrative data collected by Statistics Denmark with information on the entire 1979–1986birth cohorts in Denmark. The administrative data were collected from a number of different datasources, and as a result we have an exceptionally extensive dataset at hand for our analyses. First, thedata include detailed information on the characteristics of the 1979–1986 cohorts, including the exactdate of birth, the size of the transfer received in a given year, the high school GPA, and extensiveinformation on parents, including level of education and income. Second, detailed event history dataon education provide information about the exact time of enrollment and completion of high school,and the type of high school track attended. Finally, the data include measures of monthly labor marketparticipation (LMP). The main results will be based on the information on monthly LMP, which stemsfrom monthly reports submitted to the tax authorities by companies reporting which employees receivedpay in any given month. The data are not particularly detailed, but the information about whether anadolescent worked in a given 14 month or not is considered highly reliable. The measures of LMPare described in more detail in Section 4.3. The primary measure of academic performance is highschool GPA.15 In addition, the following outcomes are considered: the choice of advanced math, theprobability of enrolling in higher education within 2 years of high school graduation, and the probabil-ity of dropping out after turning 18.

4.1. Sample Selection

In order to avoid the estimation period coinciding with reforms of the public student transfer system,we focus on the 391,121 individuals born between 2 December 1979 and 30 January 1986. Table Iprovides an overview of the sample selection process. Administrative data on date of birth are highlyaccurate, but one exception is the date of birth of children born outside of Denmark. It turns out thatthere are more immigrants born on the first of each month than on any other day. Anecdotal evidencesuggests that this happens if immigrants, upon arrival in Denmark, are not able to provide an exact dateof birth. The caseworker will list a best guess of a date, which will often be the first of a month.Because this is a violation of our identification assumptions, immigrants were subsequently droppedfrom the sample. We focus on individuals who enrolled in a 3-year high school education and whoturned 18 during the first or second year of high school.16 Since the transfer is given under the condi-tion of high school attendance, we require that individuals turn 18 while attending high school. Fur-thermore, to be able to measure comparable post-treatment outcomes for all individuals in thesample, we disregard individuals who turn 18 during their third year of high school.

With respect to sample selection, an important issue relates to the handling of high school dropouts.If the probability of dropping out differs for the control and treatment groups, and dropouts areexcluded from the sample, the fundamental assumption of smoothness in the outcome variables inthe absence of treatment no longer holds. Inclusion of high school dropouts poses a problem withrespect to the measurement of outcomes. For dropouts, the high school GPA is unobserved. Labor mar-ket measures are observed regardless of high school attendance, but including dropouts could introducemore variance in the labor market measures since dropouts are likely to work substantially more. Wechose to handle this by excluding individuals who drop out of high school prior to their 18th birthday

14 Any individual who receives any pay during a given month is coded as participating in the labor market irrespective of thenumber of hours worked.15 The high school GPA is generally computed based on grades given in courses taken in the final year of high school. Both thegrades for the year’s work and the grades obtained at exams are included. The grades given out on the grading scale used inDenmark at that time were: 00, 03, 5, 6, 7, 8, 9, 10, 11, and 13. Grades greater than or equal to 6 are passing grades.16 The school year is assumed to run from August to July.



from the sample. If students are not forward looking in the sense that they are unfamiliar with the exactamount of transfers received after turning 18, it will not affect their dropout decision prior to turning18. In Section 5 we verify that there is no effect of treatment on the probability of dropping out priorto turning 18. Individuals who drop out after turning 18 remain in the sample since this is unequivo-cally a post-treatment decision. Specifically, we disregard individuals who drop out of high schoolprior to or during the quarter in which they turn 18.17

The maximum window on either side of the discontinuity point considered is 30 days, and we dropindividuals from the sample not born in the last 30 days or the first 30 days of a quarter. Thus, as indi-cated earlier, the sample comprises individuals born in one of the following four ‘seasons’: December–January, March–April, June–July, and September–October. There is no evidence suggesting thatdiscontinuities exist in parental characteristics, biological influences, or the like, by date of birth. How-ever, institutional features may create discontinuities in child outcomes. A common example regards therules regarding the age at school entry (e.g. Black et al., 2011). In Denmark, the rules—albeit somewhatflexible—are such that individuals born in December will tend to start school 1 year earlier thanindividuals born in January. To avoid introducing a school entry bias in the estimated treatment effect,all individuals born in December and January are dropped from the analyses. This leaves us with62,524 observations: the work estimation sample. Finally, high school GPA is only observed for about92% of the sample (57,564 observations: the GPA estimation sample ). Dropouts, whose GPA isnaturally missing, explain 87% of the missing GPAs, leaving the remaining 13% unexplained. If eitherdropout behavior or the propensity to have a missing GPA differs across the treatment and controlgroups, the estimated treatment effects will be biased. In Section 5 we establish that there is no signif-icant effect of treatment on the probability of being in the GPA estimation sample and thus verify thevalidity of the research design with respect to these issues.

4.2. Descriptive Statistics

We will refer to individuals born within the last N days of a quarter, i.e. the last N days of March, June,and September, as the treatment group for a given N-day sample. Correspondingly, individuals bornwithin the first N days of a quarter, i.e. the first N days of April, July, and October, will be referred toas the control group. Table II shows the means of outcome variables and control variables for the treat-ment and control groups in both the 30-day and 15-day work estimation samples. For both samples,

17 Dropout behavior is primarily driven by calendar time in our sample. Therefore handling the treatment and control groupssymmetrically in terms of time spent in high school is essential. Consequently, we disregard individuals from the treatment groupwho drop out during the quarter following the quarter they turn 18.

Table I. Sequential overview of sample selection

Number of individuals Percentage of total

Born between 2 December 1979 and 30 January 1986 391,121 100.0Non-immigrants 320,695 82.0Enrolled in a 3-year high school education 164,882 42.2Turned 18 during the first or second year of high school 134,615 34.4Did not drop out prior to or in the quarter in which they turned 18a 122,179 31.2Born in the first 30 days or the last 30 days of a quarter 82,708 21.1Not born in December or January 62,524 16.0Observed GPA 57,564 14.7

aTo obtain comparable treatment and control groups, we also disregard individuals in the treatment group who dropped out in thequarter in which their control group turned 18.



the treatment group receives a transfer which, on average, is approximately DKK 4500 (about USD560) higher than that received by the control group in the year they turn 18. The treatment and controlgroup means also vary across labor market outcomes, but not for high school GPA. LMP and numberof months worked are higher on average for the control group than for the treatment group. Comparingthe means of the individual and parental characteristics, we find that the treatment and control groupsare highly similar, as is essential for the validity of the empirical analysis.

Table II. Comparison of means in the control and treatment groups

30-day sample 15-day sample

TreatmentMean/SDa

ControlMean/SD

TreatmentMean/SD

ControlMean/SD

Annual transfer in 2000 in DKKb 9,954.568(5,250.922)

5,454.976***

(4,310.892)9973.950

(5,247.520)5456.919***

(4,334.858)OutcomesLabor market participation 0.800 0.817*** 0.798 0.813***

Number of months worked 6.625(4.814)

6.832***

(4.765)6.605

(4.817)6.825***

(4.775)High school GPAc 8.201

(0.952)8.203

(0.952)8.197

(0.954)8.203

(0.945)Advanced mathc 0.496 0.497 0.497 0.504Drop out of high school after 18th birthdayc 0.070 0.070 0.071 0.070Enrollment in higher educationc 0.593 0.597 0.594 0.600Yearly earnings at age 18 21,906.970

(19,069.340)22,419.600***

(18,517.420)21,902.090

(19,118.430)22460.680***

(18,577.170)Individual characteristicsFemale 0.551 0.549 0.553 0.549Turned 18 during 1st year of high school 0.434 0.444 0.442 0.438Attended 10th grade 0.606 0.590*** 0.613 0.591***

High school trackMath and science 0.370 0.374 0.373 0.374Languages 0.279 0.280 0.281 0.279International 0.001 0.001 0.002 0.001Business 0.261 0.255 0.256 0.258Technical 0.089 0.089 0.089 0.088Parental characteristicsMother, missing in data 0.000 0.000 0.001 0.000Father, missing in data 0.011 0.008*** 0.010 0.009Log of mother’s income at age 18 d 12.078

(1.913)12.094(1.896)

12.082(1.906)

12.077(1.943)

Log of father’s income at age 18 d 12.122(2.836)

12.162(2.775)

12.137(2.807)

12.141(2.829)

Mother’s income missing 0.021 0.021 0.021 0.022Father’s income missing 0.050 0.048 0.049 0.049Mother’s education levelBasic 0.251 0.250 0.250 0.250Vocational 0.335 0.329 0.335 0.328Higher 0.406 0.414 0.407 0.413Missing 0.008 0.007 0.008 0.009Father’s education levelBasic 0.215 0.205*** 0.215 0.205Vocational 0.403 0.406 0.403 0.402Higher 0.361 0.371*** 0.361 0.375Missing 0.022 0.017*** 0.021 0.018Number of observations 31,115 31,409 15,677 15,922

aStandard deviations are in parentheses. Asterisks indicate statistically different from the mean of the treatment group at ***1%level.bThere are 24 (15-day sample) and 44 (30-day sample) observations with missing information on the annual transfer.cSee Table V for sample sizes.dParental log income has been set equal to zero if missing.eIn addition to variables included in this table, specifications with controls also include indicators for year of high school enroll-ment, region of high school, number of children of the mother and age of parents at birth. Only the mean of mother’s age in the30-day sample is statistically different for the treatment and control groups.



4.3. Labor Market Participation

Figure 2 shows the motivation for our measures of LMP. This graph depicts mean monthly LMP forthe control and treatment groups from about 1 year before the time of the 18th birthday to 1 year after.The vertical line projected from 0 on the horizontal axis marks the month when the individuals in thetreatment group turn 18. The construction of the measures of LMP requires paying specific attention toa couple of issues evident in this graph.18 First, a reduced transfer does not appear to result in long-termeffects, which is why we should then focus our attention to labor market measures around the monthsfollowing the 18th birthday. Second, there is a large downward change in LMP around the 18th birth-day. We hypothesize that two main factors contribute to this drop in LMP: (i) when a worker turns 18,the minimum wage an employer has to pay increases substantially; and (ii) high school studentsbecome eligible for a public transfer when they turn 18. Since we only observe monthly LMP, we needto be careful that the constructed measures of LMP do not capture these effects.The graph shows a pattern of initial similarity in the LMP in the treatment and control groups.

Briefly, prior to the month of the 18th birthday, the paths of the treatment and control groups diverge,but shortly after they converge again. Clearly, there is no reason to expect continued divergence in thetreatment and control group work measures after the month of the 18th birthday. In fact, ignoring thetreatment effect, we even expect the treatment group to have higher LMP in the months following their18th birthday, since they have had more time to search for new jobs after potentially getting fired fromtheir old ones after turning 18. Thus our estimate will be a conservative estimate of the true treatmenteffect.We will consider two measures of LMP during high school, both of which are based on the monthly

LMP data. Let labor market participation during the 12months after the 18th birthday be an indicatorvariable with the value 1 if an individual is observed to be working in one or more months during the12months after the 18th birthday. As discussed above, we use the 12 calendar months following themonth of the 18th birthday of the control group. As a corresponding measure, we define the numberof months worked during the 12months after the 18th birthday. To some extent, this allows us to lookat both the extensive and the intensive margins.

5. RESULTS

One of the attractive features of the regression discontinuity design is the straightforward graphicalrepresentation. First, we present evidence of the existence of a discontinuity in the total amount oftransfers received by plotting this variable against the distance from the beginning of a quarter to thedate of birth; see Figure 3.19 The graph in this figure shows a clear discontinuity in the total transferreceived of about DKK 4500 (USD 560). The size of the jump is higher than three times the basicmonthly transfer, since some individuals receive the means-tested supplement or the higher basic ratefor youth living on their own.In order to gain an understanding of how youth respond to changes in transfers, we estimate the

effect of transfers on measures reflecting the two main types of decisions that youth make: workdecisions and human capital investment decisions. Graphs showing the outcomes of interest plottedagainst the distance from the beginning of a quarter to date of birth can give us a rough first impressionof the results (see Figure 4). Although not as clear as the discontinuity in the amount of transfersreceived, the graphs suggest a positive jump in LMP and number of months worked at the discontinuitypoint. For high school GPA, there is no obvious discontinuity, suggesting little or no effect on GPA.

18 The overall pattern of this graph is similar across season of birth.19 For ease of exposition, the graphical analysis bundles the 18 (3� 6) discontinuities into one.



Before turning to the main analyses, we investigate whether the differences in transfers by date of birthaffect the educational decisions of youth prior to eligibility.

5.1. Responses to Transfers Prior to Eligibility

If individuals are able to anticipate the size of the transfer they will receive in the year of their 18thbirthday and take this information into account when they make decisions earlier on, the empiricalstrategy outlined in Section 3 will be invalidated. Two obvious decisions that may be affected by ananticipation of the size of the transfer include high school enrollment and the decision to drop out ofhigh school prior to the 18th birthday. A related issue concerns the fact that some individuals have amissing GPA even though they have completed high school. If this is systematically related to dateof birth, the estimated treatment effects on GPA will be biased.

.54

.56

.58

.6.6

2.6

4

Mea

n m

onth

ly la

bor

mar

ket p

artic

ipat

ion

−10 −5 0 5 10Month relative to month of 18th birthday of treatment group

Control groupTreatment group

Figure 2. Monthly labor market participation for the treatment and control groups. 1981–1985 cohorts

5000

6000

7000

8000

9000

1000

0

−30 −20 −10 0 10 20 30Distance (in days) from beginning of a quarter to date of birth

Sample size: 62480

Size of transfer

Figure 3. Size of transfer (in DKK) received in the year of the 18th birthday by time of birth (2-day bins). Scatter-plot is overlaid with fitted values and 95% confidence bands from a linear regression on date of birth, the treatment

indicator and the interaction of the two



To address these issues, Table III reports estimates of the treatment effect on the probability ofdropping out prior to the 18th birthday, the probability of being in the GPA estimation sample, andthe probability of being in the work estimation sample. By estimating the treatment effect on the prob-ability of being in the work estimation sample, we should be able to capture any imbalance between thecontrol and treatment groups caused by responses to transfers prior to eligibility. By estimating the treat-ment effect on the probability of being in the GPA estimation sample, we test for differences in the pro-pensity to have a missing GPA across the treatment and control groups caused by either dropoutbehavior or erroneous reporting. The largest estimate in absolute size is 0.4 percentage points, but theestimates are all relatively small and insignificant. Overall, this supports the validity of the proposed

.79

.8.8

1.8

2.8

3

−30 −20 −10 0 10 20 30Distance (in days) from beginning of a quarter to date of birthSample size: 62524

A. Labor market participation

6.5

6.6

6.7

6.8

6.9

7


B. Number of months worked

8.16

8.18

8.2

8.22

8.24


C. High school GPA

Figure 4. Work behavior and grade point average by date of birth (2-day bins). Scatter-plot is overlaid with fittedvalues and 95% confidence bands from a linear regression on date of birth, treatment indicator and the interaction

of the two



estimation approach. Whether individuals are not forward looking or simply do not react along thesemargins, we cannot say. Even though the size of the transfer can be anticipated relatively easily,individuals will typically enroll in high school about 1–2 years before becoming eligible. Thus myopiaand heavy discounting probably partly explain why we find no evidence of an effect of the transfer on,for example, the probability of being in the estimation sample, while Dearden et al. (2009) find rela-tively large effects of a transfer to 16- to 18-year-olds on school participation rates.

5.2. Transfers and Labor Market Work

5.2.1. Aggregate Measures of Labor Market ParticipationThe first column in Table IV shows our preferred results, which are local linear regression estimates ofthe treatment effects on LMP and number of months worked. We find a negative and highly significanteffect on LMP, indicating that receiving about DKK 4500 more on average decreases LMP by 1.9 per-centage points. Similarly, receiving the higher amount of transfers decreases the number of monthsworked by 0.26—corresponding to about a quarter of a month or 7–8 days.

Table IV. The effects of transfers on labor market participation

(1) (2) (3) (4)

Estimation approach Non-parametric Non-parametric Parametric Nonparametric: received morethan the basic transfer

A. Labor market participationTreatment effect �0.019***

(0.007)�0.023**

(0.010)�0.015**

(0.006)�0.029***

(0.011)R2 – – 0.038 –

B. Number of months workedTreatment effect �0.264***

(0.083)�0.274**

(0.119)�0.222***

(0.075)�0.234*

(0.128)R2 – – 0.056 –Observations 62,524 31,599 62,524 28,165Control variables – – Yes –Bandwidth (in days) 30 15 – 30

aAsterisks indicate statistical significance at the ***1%; **5%; and *10% levels. Standard errors are in parentheses.bStandard errors for nonparametric estimates are bootstrapped with 1000 replications.cFor the parametric estimation, the 30-day sample is used. Standard errors are heteroskedasticity robust.dIn addition to the variables summarized in Table II, controls include indicators for year of high school enrollment, region of highschool, number of children of the mother, and age of parents at birth.

Table III. Responses to transfers prior to eligibility

Estimation approach Nonparametric

A. Drop out of high school prior to 18th birthdayTreatment effect �0.003

(0.005)Observations 69,331

B. In GPA estimation sampleTreatment effect �0.002

(0.005)Observations 160,122

C. In work estimation sampleTreatment effect �0.004

(0.005)Observations 160,122Bandwidth (in days) 30

aAsterisks indicate statistical significance at the ***1%; **5%; and 10% levels. Standard errors are in parentheses.bStandard errors are bootstrapped with 1000 replications.



The fact that the estimates are negative is expected if we believe that youths receiving a higher trans-fer may decide to substitute some of their time spent on the labor market for time spent on leisure orschool work.Nonparametric estimates are often sensitive to the choice of bandwidth. The second column in

Table IV therefore presents the results for a bandwidth of 15 days instead of the 30 days used in the firstcolumn. This only has minor effects on the estimates, but as sample size is halved the standard errorsincrease somewhat. The third column shows the estimated treatment effect from an ordinary leastsquares regression on the 30-day sample with control variables. In this case, the linear regression yieldsalmost the same estimated treatment effects as the local linear regression.We expect individuals to have differential responses to the transfer depending on the transfer rate

they are entitled to. Since differences in the rates are mainly caused by means testing against parentalincome, estimating separate effects for this group will also be suggestive with respect to whether or notwe can expect heterogeneous responses by parental income, for example, which we will examine inmore detail in Section 5.4. For now, we focus on the group of individuals who received more thanthe basic transfer.20 The estimated treatment effects for this group are reported in the fourth column.The estimated treatment effect on LMP is �2.9 percentage points, which is consistent with the notionthat the group of individuals receiving more than the basic transfer are slightly more responsive thanthe sample as a whole. However, the estimated treatment effect on number of months worked is almostunchanged at �0.23.Overall, the estimated treatment effects are in the range of �2.3 to �1.5 percentage points for LMP

and �0.27 to �0.22months for number of months worked when we disregard the subsample ofindividuals who received more than the basic transfer. One way to quantify these results and comparethe magnitudes of the estimates to the existing literature on labor market participation is to calculate thecorresponding income elasticity of labor market participation, Z. For high school students in the sam-ple, income is likely to consist of three main components: labor market earnings, public transfers, andparental transfers. Since parental transfers are unobservable to us and only the response of LMP to arelative large change in public transfers is known, strong assumptions are needed to quantify theincome elasticity. We assume that there are no differences in labor market earnings between the controland treatment groups and set this equal to the mean value in the sample.21 The public transfers for thecontrol and treatment groups are set equal to the corresponding mean values of the sample.

22 In thecase of no parental transfers, the estimate of Z is �0.14. Erichsen (2009) estimates the average sizeof monthly parental transfers to be around USD 50 for Danish 17-year-olds. Then, in the case whereparental transfers are positive, but where differences in public transfers do not translate into differencesin parental transfers, and parental transfers cease when the child turns 18, the mean parental transferwould be roughly USD 300 (6�USD 50). This implies an income elasticity of �0.16. Finally, sup-pose that parents mitigate the effects of the transfer in the sense that individuals in the control groupreceive higher parental transfers than those in the treatment group. In this case, the estimated elasticitieswill be larger in absolute size. For example, if we assume that parental transfers cease when the ado-lescent becomes eligible for the public transfer, the control group receives parental transfers of roughlyUSD 450, while the treatment group receives roughly USD 300. In this case the estimate of Z is�0.22.Existing studies of income elasticities do not provide the most suitable benchmarks for this particular

sample of individuals. Eissa and Hoynes (2004) report income elasticities of labor market participationof �0.039 for women and �0.007 for men using the responses of married couples to expansions of the

20 Whether or not an individual received more than the basic transfer is approximated based on yearly information about the sizeof the transfer received and the number of months of eligibility.21 The mean can be deduced from Table II and corresponds to about USD 2765.22 These are reported in Table II and correspond to about USD 674 and USD 1230 for the control and treatment groups,respectively.



Earned Income Tax Credit. The income elasticities we find are actually closer to those found in Imbenset al. (1999), who use exogenous variation in income based on lotteries and report an income elasticityof LMP of�0.14. The magnitude of the estimated elasticity may reflect the fact that the labor supply ofsecondary earners is generally more responsive to changes in income than that of primary earners (see,for example, Boskin and Sheshinski, 1983). Thus we would expect the labor supply of youth attendinghigh school and living with their parents to be more elastic than that of the adult population or youth infull-time work.23

5.2.2. Monthly Measures of Labor Market ParticipationSo far, we have reported results on aggregate work measures in the 12months following the 18th birth-day. Figure 5 shows how the response to the difference in transfers varies over time; i.e. it showsestimated treatment effects on monthly LMP. Related to our discussion of the construction of labormarket measures, we see a remarkably large negative treatment effect in the month following the18th birthday. This effect is caused by the difference in calendar time between the treatment and thecontrol groups. With the exception of 2months, the estimated treatment effects are close to zero andstatistically insignificant until about 2months prior to the 18th birthday. In the first 6months afterthe 18th birthday—disregarding the first month after the 18th birthday—the estimated treatment effectsare about �0.3 to �0.4, and they decrease in absolute size over time. The pattern is similar to thatobserved in the raw data in Figure 2. Both graphs suggest that individuals are not completely myopic,but change their labor market behavior a couple of months prior to eligibility. Furthermore, the differ-ence in work outcomes between the control and the treatment groups is of a purely transitory nature.Individuals could have chosen to smooth their LMP over time in anticipation of this transfer, but theyappear to react only when close to their 18th birthday.

5.3. Transfers and Academic Performance

As the above results have made clear, labor market decisions of youths are affected by the transfergiven during high school. The next step of our analysis is to investigate whether this affects thedecisions individuals make regarding investments in their human capital. In other words, when youthsreceive the higher transfer, do they then invest more heavily in their human capital, e.g. by spendingmore time on school work, which we would expect to result in a higher GPA, or by choosing a moredemanding course load?

Table V reports the estimated treatment effects on the high school GPA, the choice of advancedmath, the probability of dropping out of high school, and the choice of college enrollment within2 years of high school graduation. The estimated treatment effects on GPA are all negative and insig-nificant. Our preferred specification suggests a small treatment effect of about �0.010. The size of theeffect corresponds to about a hundredth of a standard deviation of high school GPA. The estimatedstandard errors are sufficiently small, making it possible to reject that lowering the transfer to youthswould have any substantial adverse effects on GPA. As for labor market outcomes, parametric estima-tion yields similar estimates. Even for individuals who receive more than the basic transfer, the esti-mated effect is exceedingly small.24 If individuals with low ability are more likely to drop out and

23 We have also estimated the effect on earnings in the year of the 18th birthday. The estimated effects imply income elasticitiesof earnings in the range of �0.31 to �0.15. The results are available from the authors upon request.24 We interpret the estimated treatment effects as a zero effect on GPA. One could hypothesize why GPA may be positivelyaffected by a lowering of the transfer. Rothstein (2007) suggests that there are potentially two opposing effects at work whenconsidering the effects of high school employment on academic performance. While working may decrease the time availablefor school work, it may provide youth with valuable knowledge and skills in the labor market or increase their motivation inschool. Also, Markowitz and Tauras (2009) find that teenagers with higher incomes are more likely to engage in substanceuse such as drinking, smoking, and smoking marihuana.



increasing the transfer decreases the probability of dropping out, ceteris paribus, the estimated treat-ment effects on academic performance will be biased downwards. A conservative assumption is that1% of the individuals in the control group drop out due to the lower transfer.25If we assume that theseindividuals would have acquired a GPA of 6, which is the lowest passing GPA, the estimate of thetreatment effect would have a negative bias of the order of 0.02.The estimated treatment effects on the other academic outcomes are shown in panels B, C and D of

Table V. Taking advanced math classes is considered to be relatively time consuming and a determi-nant of future academic performance (Joensen and Nielsen, 2009).26 By considering the effects on theprobability of enrollment in higher education, we might be able to capture some forms of human capitalinvestment not captured in the other more traditional measures of academic performance.27 Individualsmay also choose to spend more time gathering information about their own ability and the nature ofspecific fields of education that will enable them to decide on a field at an earlier time. The estimatesare relatively stable across specifications and they are all insignificant at the 5% level. Overall, we findwhat we interpret to be essentially zero effects on academic performance, suggesting that although theindividuals in the treatment group receive a higher transfer and work less, they do not substitute theirtime towards investments in human capital accumulation.

5.4. Heterogeneous Responses to Transfers

So far the analysis has focused on estimation of the average treatment effect for the entire sample. However,it is likely that young individuals with different characteristics would respond differently to treatment. If thelabor market behavior of specific groups is more responsive to changes in the transfer, considering the effectsof the transfer on academic performance for these groups is also of interest. Table VI presents the estimatedtreatment effects on LMP, number of months worked, and GPA for various subgroups. In addition, wepresent estimates of the effect of a DKK 1000 increase in transfers since the average treatment differs

25 The lower 95% confidence limit on the estimated treatment effect on the probability of dropping out is about �1 percentagepoint (cf. Table V).26 Students typically choose advanced math during their second year of high school, implying that many individuals in the sam-ple would already have been receiving cash transfers at that point.27 For the estimation with college enrollment within 2 years of high school graduation, we only include the 1980–1983 birthcohorts. Obviously, this measure is conditional upon high school graduation. If the treatment effect on the probability of dropoutwere nonzero, then the control and treatment groups would no longer be balanced.

−.0

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−.0

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0.0

2T

reat

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t effe

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−10 −5 0 5 10Month relative to month of 18th birthday of treatment group

Figure 5. Nonparametric estimates of treatment effects on monthly labor market participation and 95% confidencebands. Weighted average of the season and year-of-birth specific treatment effects. 1981–1985 cohorts



across subgroups.28 This enables us to explicitly determine whether some groups are more responsiveto a given change in the transfer than others. For each estimated treatment effect, we test whether theestimate is significantly different from the corresponding estimate of the reference group. Even thoughthe standard errors are relatively large, the estimates of the subgroup treatment effects reveal some in-teresting patterns.

Since the majority of the youths in our sample are still a part of their parents’ household, we expect thatthe treatment effect is likely to vary across individuals with different parental backgrounds. Parents with astrong socioeconomic backgroundmay provide intra-household transfers to children to a wider extent thanparents with more disadvantaged backgrounds. We focus on two indicators of parents’ socioeconomicbackground, namely the father’s education level and parental income. The estimates of the treatment effectby the fathers education level do not reveal a clear pattern. Individuals whose fathers only have a basiceducation tend to be more responsive to treatment in terms of LMP, but not particularly so with respectto number of months worked. The small, negative estimate of the treatment effect on GPA presented inTable V seems to be driven by individuals whose fathers have vocational qualifications.

A clearer pattern emerges when we consider the subgroups related to the financial capabilities of theparents.29 As we expect, young individuals whose parents have lower income tend to be more

28 The estimate is a nonparametric estimate of the ratio of the difference in outcomes and the difference in transfers between thetreatment and the control groups. This is similar to the IV estimate obtained from a regression of the outcome of interest on thesize of the transfer using treatment status as an instrument.29 Parental income quintiles are based on the entire cohort of youth and not just youth who enroll in high school.

Table V. The effect of transfers on academic performance

(1) (2) (3) (4)

Estimation approach Non-parametric Non-parametric Parametric Nonparametric: Received morethan the basic transfer

A. GPATreatment effect �0.010

(0.017)�0.003(0.024)

�0.013(0.015)

�0.028(0.025)

R2 – – 0.105 –Observations 57,564 29,074 57,564 25,586

B. Advanced mathTreatment effect �0.015

(0.011)�0.025(0.016)

�0.009(0.008)

�0.018(0.017)

R2 – – 0.377 –Observations 38,206 19,319 38,206 15,891

C. Enrollment in higher education within two yearsTreatment effect �0.017

(0.011)�0.028*

(0.016)�0.017*

(0.010)�0.011(0.016)

R2 – – 0.077 –Observations 38,830 19,563 38,830 17,361

D. Drop out of high school after 18th birthdayTreatment effect �0.002

(0.004)�0.004(0.006)

�0.002(0.004)

0.010(0.009)

R2 – – 0.048 –Observations 62,524 31,599 62,524 20,020Control variables – – Yes –Bandwidth (in days) 30 15 – 30

aAsterisks indicate statistical significance at the ***1%; 5%; and 10% levels. Standard errors are in parentheses.bStandard errors for nonparametric estimates are bootstrapped with 1000 replications.cFor the parametric estimation, the 30-day sample is used. Standard errors are heteroskedasticity robust.dIn addition to the variables summarized in Table II, controls include indicators for year of high school enrollment, region of highschool, number of children of the mother, and age of parents at birth.eWe use information on parental income to predict who would have been entitled to more than the basic transfer, since the trans-fer received may be unobserved for dropouts.fSamples are adjusted as follows: for the choice of advanced math, only individuals enrolled in the ‘math and science’ or ‘lan-guage’ track are included. In addition, individuals who complete high school after 2005 are not included. Forthe choice of enroll-ment in higher education only the 1980–1983 cohorts and individuals who complete high school are included.



responsive to the transfer. The estimated treatment effects on work behavior tend to be larger at lowerquintiles, although there are some minor irregularities in this pattern. A DKK 1000 increase in transfersdecreases LMP by 1.2 percentage points more for youth in the bottom income quintile compared tothose in the top income quintile. Although the overall pattern suggests that individuals from low-in-come families are more responsive to changes in the transfer, we find no corresponding increase inGPA for these groups. The finding that youth from low-income families adjust their labor marketbehavior and thereby their earnings suggests that at least some of these youth are indeed borrowingconstrained.30

5.5. Choice of Bandwidth

The choice of bandwidth is potentially extremely important for the nonparametric estimation results.As a result, we perform a robustness check on our three main outcomes: GPA, LMP, and number ofmonths worked. Figure 6 shows the estimates and the 95% confidence intervals obtained using thenonparametric estimator. For bandwidths of about 7–10 days and above, the results do not changemuch. Because we expect the estimates to be more imprecise at the low bandwidths, we consider theseresults a good indicator that our choice of bandwidths (15 and 30 days) are reasonable. These

30 We have also estimated heterogeneous effects for gender, work prior to the 18th birthday, mother’s education, and parentalwealth. All estimates are insignificant except those for parental wealth. The results are available from the authors upon request.

Table VI. Heterogeneous Responses to transfers

Outcome Treatment effect Effect of a DKK 1000 increase in transfers

GPA Labor marketparticipation

Number ofmonths worked

GPA Labor marketparticipation

Number ofmonths worked

A. Father’s educationBasic (ref.group)

0.014(0.037)

[11,843]

�0.049(0.015)

[13,136]

�0.244(0.185)[13,136]

0.003(0.008)

[11,834]

�0.010(0.003)

[13,125]

�0.049(0.038)[13,125]

Vocational �0.023(0.027)

[23,065]

�0.014*

(0.010)[25,291]

�0.278(0.124)[25,291]

�0.005(0.006)

[23,056]

�0.003*

(0.002)[25,278]

�0.060(0.026)

[25,278]Higher 0.006

(0.028)[21,586]

�0.013*

(0.013)[22,872]

�0.285(0.139)[22,872]

0.001(0.007)

[21,574]

�0.003(0.003)[22,854]

�0.065(0.032)[22,854]

B. Parental incomeQuintile 1(ref.group)

�0.023(0.053)[6,258]

�0.063(0.022)[7,165]

�0.485(0.257)[7,165]

�0.004(0.009)[6,251]

�0.011(0.004)[7,153]

�0.081(0.042)[7,153]

Quintile 2 0.029(0.042)[8,606]

�0.035(0.018)[9,519]

�0.079(0.215)[9,519]

0.006(0.008)[8,604]

�0.007(0.004)[9,515]

�0.016(0.042)[9,515]

Quintile 3 �0.010(0.038)

[10,985]

�0.025(0.015)

[11,979]

�0.322(0.184)[11,979]

�0.002(0.009)

[10,981]

�0.005(0.003)[11,975]

�0.070(0.042)[11,975]

Quintile 4 �0.024(0.034)

[14,297]

�0.020(0.014)[15,396]

�0.246(0.162)[15,396]

�0.006(0.008)

[14,291]

�0.005(0.003)[15,389]

�0.056(0.039)[15,389]

Quintile 5 0.014(0.032)

[17,285]

0.006***

(0.013)[18,316]

�0.287(0.157)[18,316]

0.003(0.007)

[17,276]

0.001**

(0.003)[18,305]

�0.069(0.036)[18,305]

aAsterisks indicate statistical significance at the ***1%; **5%; and *10% levels for the null of equality between thegroup and the reference group. Standard errors are in parentheses. Number of observations is in square brackets.bAll reported estimates are nonparametric using a bandwidth of 30 days. Standard errors are bootstrapped with 1000 replications.cThe cutoffs for the income quintiles are approximately (in DKK 1000): 377, 481, 569, and 702.



bandwidths give us enough observations to obtain informative estimates while using observations rel-atively close to the discontinuity point.31

6. CONCLUSION

We provide valid evidence of the causal effect of transfers given to adolescents conditional on school-ing. The analysis is based on large administrative datasets with extensive information on the 1979–1986birth cohorts in Denmark. In order to identify a causal effect of transfers on the labor market behaviorand academic performance of youths, we exploit the fact that the total transfer received varies by dateof birth. We find that an increase in the transfer decreases labor market participation and number ofmonths worked. The estimated income elasticity of labor market participation is in the range of

31 We have also experimented with the cross-validation procedure described in Imbens and Lemieux (2008). Similar to Ludwigand Miller (2005), we find that the estimated loss function is extremely flat, which means the procedure does not seem particu-larly well suited for optimal bandwidth selection in our application.

−.1

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Bandwidth

High school GPA

−.0

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.04

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Tre

atm

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ffect

5 10 15 20 25 30Bandwidth

Labor market participation

−.6

−.4

−.2

0.2

.4T

reat

men

t effe

ct

5 10 15 20 25 30Bandwidth

Number of months worked

Figure 6. Nonparametric estimates of treatment effect and 95% confidence bands for bandwidths in the range of5–30 days. Weighted average of the season and year-of-birth specific treatment effects



�0.22 to�0.14. Our findings suggest that the transfer has a negligible effect, if any, on measures of ac-ademic performance, e.g. the high school GPA.When we estimate treatment effects by parental income, we find that individuals from families with

lower incomes tend to be more responsive to an increase in transfers. We find that for youth in the bot-tom income quintile, a DKK 1000 increase in transfers decreases LMP by 1.2 percentage points morethan for those in the top income quintile. Thus our findings suggest that the labor market decisions ofindividuals from lower-income families are more responsive to changes in the transfers thanindividuals from higher-income families. Nonetheless, we find no corresponding effects on academicperformance for individuals from lower-income families.Our results contrast with the literature on conditional cash transfers, which generally tends to find

these types of transfers particularly suitable for achieving policy goals. While conditional cash transfersmay be highly effective in developing countries, this is not necessarily the case in developed high-in-come countries.To our knowledge, this paper is the first to analyze the effect of universal conditionalcash transfers to youth in a high-income welfare state. Our results suggest that the transfer does noteffectively increase academic performance, but that it does affect the labor market decisions of youths.In particular, the labor market behavior of youths from economically disadvantaged families appears tobe affected. The results are consistent with the presence of borrowing constraints for adolescents. Thefact that the cash transfer for high school students is neutral with respect to educational outcomessuggests that this universal public transfer program simply allows recipient households to increase con-sumption of other goods. Thus the actual effects of the implemented transfer program are not closelyaligned with the stated objectives of policymakers.A crucial aspect of our empirical setup is that individuals do not respond to the increase in transfers

prior to eligibility. Our analysis verifies that the responses in terms of labor market behavior are indeedfocused around the time of eligibility. Moreover, the decision to enroll in high school and stay in highschool prior to eligibility appear to be largely unaffected by the differences in transfers. This is contraryto results found by Dearden et al. (2009), who find substantial effects of a conditional cash transfer toadolescents on participation rates. However, the timing of the transfer in our application is such thatdecisions regarding enrollment and dropout are usually made a considerable amount of time beforebecoming eligible for the transfer. We hypothesize that myopia and high discount rates for youth implythat the individuals in our sample do not respond along these margins. Even though Dearden et al.(2009) use a significantly different sample, their results support the idea that the specific design andimplementation of the transfer system are crucial for the results obtained. In contrast to the cash trans-fer studies by Dearden et al. (2009), which is much more aligned in time with the relevant decisions ofthe youth, the transfer we consider is potentially not received until years after the decision has beenmade to enroll in high school. As a result, designing transfer programs so there is greater alignmentwith the policy goals may improve the effectiveness of such programs.

ACKNOWLEDGEMENTS

An earlier version of this paper was circulated as ‘The effects of financial aid in high school on aca-demic and labor market outcomes: a quasi-experimental study’. Maria Knoth Humlum is grateful forfinancial support from the Danish Strategic Research Council project, ‘Intergenerational Trans- missionof Human Capital’. We have benefited from constructive comments from participants at the DGPE 2008workshop, the SFI workshop on Applied Microeconomics and Program Evaluation, the ESPE 2009conference, the Danish Microeconometric Network Meeting 2009, the EALE/SOLE 3 rd InternationalConference 2010, and seminar participants at Aarhus University and AKF. In addition, we would liketo thank the editor (Edward Vytlacil), three anonymous referees, Torben M. Andersen, Jacob NielsenArendt, Paul Bingley, Lance Lochner, Helena Skyt Nielsen, Marianne Simonsen, Michael Svarer, ChrisTaber, and Allan Wu¨rtz for many valuable comments. The usual disclaimer applies.



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THE RESPONSES OF YOUTH TO A CASH TRANSFER ...faculty.smu.edu/millimet/classes/eco7377/papers/humlum...intra-household transfers mitigates the observed effects of the transfer. Nonetheless,