Labour Economics 25 (2013) 1–11

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Labour Economics

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Financial incentives and study duration in higher education☆

Trude Gunnes ⁎, Lars J. Kirkebøen, Marte RønningStatistics Norway, Research Department, Postboks 8131 Dep., N-0033 Oslo, Norway

H I G H L I G H T S

• From 1990–1995 certain students in Norway received a reward for on-time completion.• Mean delay was reduced by 0.23 semesters per year treated.• Some indication that treatment should start before the final part of studies.• Earnings while studying decreased slightly; no effects on longer-term earnings.• On-time graduation increased from a low level, thus cost to treat relatively low.

☆ We are grateful for generous comments from Hans BoTorbjørn Hægeland, Edwin Leuven, Helena Skyt Nielsen, OPer Tovmo, Roope Uusitalo, Kjell Vaage and two anonymthe II IEBWorkshop on Economics of Education, the 18th Ience, and the EALE 2012 conference. The usual disclaimer⁎ Corresponding author.

E-mail addresses: gut@ssb.no (T. Gunnes), kir@ssb.n(M. Rønning).

0927-5371/$ – see front matter © 2013 Elsevier B.V. Allhttp://dx.doi.org/10.1016/j.labeco.2013.04.010

a b s t r a c t

a r t i c l e i n f o

Article history:Received 31 October 2012Received in revised form 20 April 2013Accepted 23 April 2013Available online 1 May 2013

Keywords:Financial incentivesHigher educationOn-time graduationSemesters delayedDifference-in-difference

This paper investigates to what extent students in higher education respond to financial incentives byadjusting their study behavior. Students in Norway who completed certain graduate study programs be-tween autumn 1990 and 1995 on stipulated time were entitled to a restitution of approximately 3000 USDfrom the Norwegian State Educational Loan Fund. Comparing treated and untreated (control) programs ina difference-in-differences framework, we find that the average delay in the treatment group decreased by0.8 semester during the reform period, and by 1.5 semesters in the following two years. Number of yearstreated matters strongly, with delays reduced by 0.23 semesters per year treated. Furthermore, there issome indication that it is important that treatment starts before the final part of the educational programs.The share of on-time graduation increases by 3.8 percentage points per year treated, from a pre-reformlevel of about 20%. Thus, a large share of the restitutions given will be for students who would otherwisenot have graduated on time. A series of robustness checks indicate that our estimated effects do not reflectdifferential trends or omitted variables.

© 2013 Elsevier B.V. All rights reserved.

1. Introduction

Because education is believed to have positive externalities, and asa way to promote equality of opportunity, higher education is subsi-dized in many countries. This is the case whereby students do notpay the full cost of their instruction through tuition, or when livingexpenses are partly covered either through scholarships, or throughfavorable student loans provided by government agencies.

nesrønning, Robert Gary-Bobo,ddbjørn Raaum, Bjarne Strøm,

ous referees and participants atnternational Panel Data Confer-s apply.

o (L.J. Kirkebøen), mro@ssb.no

rights reserved.

From human capital theory, we would expect subsidies to increasethe net return to education and help to offset credit constraints. How-ever, the presence of subsidies to education may not only increasestudents' attainment level, but also influence the level of effort pro-vided by students. As students are generally subsidized for each unitof time spent studying, and not for the degree attained, there maybe incentives to spend too much time in the educational system.This may for instance be the case if the consumption value, i.e., theprivate, non-pecuniary return to education, is a dominant factor for thestudents' choice of study duration (Alstadsæter and Sivertsen, 2010;Zafar, 2009). Consequently, a higher level of student supportmayfinanceincreased consumption of higher education, with few externalities.

It is indeed observed that many students enrolled in universitiesand college programs around theworld do not complete their universityor college degree on time. According to the U.S. Department of Education(2003), first-time recipients of bachelor's degrees between 1999 and2000 spent on average 10 extra months finishing their degree beyondthe estimated completion time. Similar patterns are documented for

1 The single important exception to this rule is a private business school that ac-counts for about 10% of the students and charges significant tuition fees.

2 Source: This figure and the following figures concerning loans and grants aretaken from the website of the Norwegian State Educational Loan Fund, http://www.lanekassen.no/, unless stated otherwise.

2 T. Gunnes et al. / Labour Economics 25 (2013) 1–11

many European countries (Brunello and Winter-Ebmer, 2003). This re-sult, together with the general belief that students do not exert sufficientstudy effort, has increased policy makers and researchers' interest inwhether students respond to financial incentives.

This paper studies the effects of financial incentives on study dura-tion using rich register data to investigate the effect of a reform thatrewarded students who completed their higher education degreenominally on time. The reform entitled students in Norway who com-pleted certain graduate study programs between the autumn semes-ter of 1990 and the autumn semester of 1995 to a restitution from theNorwegian state educational loan fund of approximately 18,000 NOK(about 3000 USD) if they finished the program on nominal time.Thus, the reform created clear differences in the financial incentivesthat the autumn 1990 to 1995 graduation cohorts faced comparedto previous and subsequent cohorts. These differences are exploited toestimate the impact of the financial reward on study duration. The factthat students enrolled in some education programs were not eligiblefor the restitution provides an additional comparison group that allowsa difference-in-differences approach that can control for confoundingtime effects.

This reform was among the first to focus on the intensive margin,explicitly aiming at improving students' study effort and the efficiencyin higher education. Earlier reforms had only been concerned with thedesign of students' support system (loans and grants) related to theextensive margin, such as increasing enrollment and access to highereducation by providing a subsidy to all students independent of perfor-mance. A majority of the empirical literature on study duration inhigher education focuses on the latter. Dynarski (2003, 2004) finds sub-stantial effects of changes in student aid on college attendance in the US.Nielsen et al. (2010) and Baumgartner and Steiner (2005) find smallereffects, studying respectively Danish and German reforms. However,Denmark already had substantial student aid, and the German reformonly targeted low-income families.

More in line with our study, the potential of financial incentives toincrease students' study efficiency and performance has also attractedsome attention. Leuven et al. (2010) implement a randomized exper-iment among first-year students at the University of Amsterdamwhere those who passed all of their courses on time could earn acash reward. They find increased performance for higher-ability stu-dents, but a reduction for less able students. Garibaldi et al. (2012)study discontinuities in tuition at the Bocconi University in Italy, find-ing that higher tuition reduces the probability of late graduation.Hakkinen and Uusitalo (2003) evaluate a Finnish reform that wasintended to shorten study duration by replacing loan-based student aidwith a system of grants. The reform had only a modest effect, most ofthe decline in the time to degree can be explained by an increase in theunemployment rate that reduced student employment opportunities.Heineck et al. (2006) apply a duration analysis to examine the effectson studyduration of an additional tuition fee for students enrolled in uni-versity programs (in Germany) beyond the regular completion time.Their findings are ambiguous.

This paper contributes to the literature by being one of the few pa-pers addressing the causal effect of financial incentives on study dura-tion among students in higher education. Moreover, it includes thewhole student population in Norwegian higher education institu-tions. Previous papers with a credible research design have typicallyonly focused on students fromone particularfield of study or university.It is also the first paper to directly address number of semesters delayedas dependent variable (previous papers have focused on graduation ontime or student achievement). In addition, we look at the timing of theincentive to address the importance of late versus early treatment. Fol-lowing other papers, such as Joensen (2011) and Humlum and Vejlin(2011), we also investigate whether earnings from part-time workwhile studying is affected.

The remainder of this paper is organized as follows: Section 2 pro-vides some background on the higher education system in Norway, as

well as the student support system and the incentive reform, i.e., theturbo reform. It also highlights some of the potential mechanisms forstudents to adjust their study duration. Section 3 presents the data,while Section 4 outlines the empirical strategy. Section 5 presentsthe findings and Section 6 offers some conclusions.

2. Institutional settings and the “turbo” reform

2.1. Higher education in Norway

The Norwegian higher education sector is almost completely dom-inated by public institutions, which have 85% of enrolled students.Tuition fees are virtually zero, making the direct costs of higher edu-cation very low.1 There are three different types of higher educationinstitutions: universities, specialized university colleges and regional uni-versity colleges. During the 1990s, most students at regional universitycolleges enrolled in two- or three-year professionally oriented programs(e.g., nursing, teaching, engineering and commerce), whereas students inspecialized university collegesmostly enroll in four- to six-year programsin specializedfields, such as business, architecture and veterinary science.Universities offered two tracks: integrated five- or six-year programsleading to a graduate degree, or shorter programs in different fields thatcould be combined to eventually earn a Master's degree. This latterstudy program bears some resemblance to the American universitysystem, although there was no “core curriculum” for undergraduates inNorway. Students in Norway who wished to begin a graduate programhad to complete a related undergraduate program.

2.2. The Norwegian state educational loan fund

The Norwegian state educational loan fund offers favorable loansto students who enroll in higher education programs. The loan sup-port, which is meant to cover the students' costs of living during thestudy period, is favorable in several respects. No interest is calculatedand no repayment is required until the education is completed. Also,the loan may be fully or partially waived if insufficient income aftercompleted education. In the case of death, the loan is waived.

The Norwegian Parliament decides every year how much moneyto assign to students during the subsequent school year, generallyadjusting this amount to keep up with students' costs of living. Thissum, which amounted to 54,000 NOK (about 9000 USD) for the1991/1992 academic year (where about 42,000 NOK was given asloans, and 12,000 NOK as grants), is the same for all students and isnot affected by parental income.2 On the other hand, the financialsupport depends on students' own income and wealth.

The fraction of students in higher education who take up loans isclose to 100% (Berg, 1997). In 1994 the average loan amount per studentwas approximately 155,000 NOK for students completing higher educa-tion (both shorter and higher degrees). The average loan is likely to behigher for the students we consider as they all have higher degrees.

The situation in Norway is in contrast to other countries. For in-stance, despite favorable conditions, the take-up rate of student loansin the Netherlands is low (Booij et al., 2012). One explanation for theirfindings may be debt aversion in addition to cognitive constraints.

2.3. The “turbo” reform

Students in Norway who completed certain graduate educationprograms between autumn 1990 and autumn 1995 were entitled to

3T. Gunnes et al. / Labour Economics 25 (2013) 1–11

restitution from the Norwegian state educational loan fund if theygraduated on the stipulated time. The restitution was 18,000 NOK(about 3000 USD) and corresponded to about 10% of the total loanamount (for an average student). The proposed budget was madepublic in October 1990, and passed in November/December. The re-form was introduced in the regulations for the state educationalloan fund from July 1991, but students graduating on the stipulatedtime in autumn 1990 and spring 1991 could also benefit from thenew incentive scheme.

The termination of the reform was announced in summer 1995,and the last students who could benefit from the reform was theautumn 1995 graduation cohort. During the reform period, financialsupport for students was debated in the Norwegian Parliament. Al-though the debate mostly focused on interest rates and general grantlevels, the reformwas proposed to be discontinued in the 1994NationalBudget, but at that time continued by the national assembly. It maytherefore be unclear what expectations students during the reform pe-riod had about the future of the reform. Newspaper reports suggest thatstudents were surprised by the discontinuation of the reform. Further-more, the Norwegian state educational loan fund, which is the mainprovider of such type of information to students, first announced thedissolution of the reform in the summer of 1995.

The autumn 1990 to autumn 1995 graduation cohorts faced in-creased incentives to complete their studies on time compared toprevious and subsequent cohorts. We will exploit this to estimatethe impact of financial reward on study duration. As the autumn1990 graduates had little time to respond to the changed incentives,we denote the period from spring 1991 to autumn 1995 as thetreatment period. Conveniently for our analysis, students in someeducation programs were not eligible for the restitution (seebelow). This rule provides a comparison group that can be used ina difference-in-differences approach that corrects for confoundingtime effects.3

4 When higher education can be financed through favorable loans and grants, work-ing while studying appears inefficient in terms of expected lifetime income as workingdelays labor market entry. However, working while studying may generate returns in

2.4. What should we expect of this reform?

From incentive theory, we know that incentives are more likelyto be effective when the award is given on shorter terms(Holmström and Milgrom, 1987). In addition, the form taken bythe subsidy itself – no direct cash reward, but a loan reduction –

may be perceived as a somewhat low-powered incentive. On theother hand, students may be more financially constrained. Hence, areduction in loan of 18,000 NOK (about 3000 USD) may be a sizablereduction for this particular group. Additionally, the potential psychiccost of debt (debt aversion) may cause students to respond morestrongly to a debt reduction than a corresponding income increase. Fur-thermore, if study duration is something students can easily influence(relative to for instance academic performance, which may to a largerextent depend on endowed ability), students can respond even to amoderate incentive.

The motivation for the reform was a belief that excess time tograduation reflected sub-optimal effort from the students. However,in addition to increased effort, students could also respond by increas-ing time spent on studying, or by graduating with less skills. Changesin the effort provided by students are unobserved. We will thereforelook at changes along the two latter margins in order to say somethingabout the underlying mechanisms.

3 From 1988 to 2003, students who opted for any longer study programs lasting 10-to 13-semesters were entitled to another restitution that was not linked to time to de-gree, but degree completion. The restitution was increasing with the length of thestudy program, ranging from around 19,000 NOK for 10-semester programs to46,000 NOK for 13-semester programs. However, as this reform affected all studentsequally, we do not expect it to bias our difference-in-differences estimate.

Oneway for students to increase study hours could be to reduce lei-sure, which we cannot observe. Another way is to reduce part-timework.4 Arendt (2012) exploits a large scale Danish reform that, amongother things, increased student grants by 3000 USD per year. This re-form had the intended effects of increasing the take-up of studentgrants, reducing student drop-outs and lowering work hours whilestudying. As our reform corresponds to a total sum of 3000 USD inloan reduction after at least five years of studying, we expect a smallereffect on students' work. Nevertheless, in the empirical part of thepaper, we will take a closer look at whether the reform caused studentsto adjust their part-time work.

An alternative student response could be to graduate on time, butwith less skills, i.e., lower grades. Unfortunately, we do not have anydata on grades. As a proxy for skills we therefore use earnings aftergraduation. It is however important to keep in mind that earning mayalso reflect other characteristics than students' achievements in school.

There is also a possibility that the reformunder studymay discouragesome students, increasing delays, or causing non-completion. As it willbe documented, many students have long delays and few studentsactually graduate on time. This could cause the reform to discourage stu-dents that are far from reaching the target.5 If students are discountingthe future, they will react more the closer they get to completion time.Students who are only treated at the end of their study (partly treated)may hence be discouraged if they are not able to catch up due to earlydelays generated before entering the treatment period. On the otherhand, as the reform seeks to induce good study habits and steady studyprogression from the start (otherwise it would not work as delays arehard to rebound), students who are treated during their whole studyperiod should be less likely to delay their studies, and hence less likelyto be discouraged. With our data we are able to shed some light on thepotential discouragement effect by differentiating between fully treatedand partly treated students.

3. Data and descriptive statistics

We use register data from Statistics Norway, consisting of all stu-dents who were predicted (or expected) to graduate from Norwegianhigher education institutions between 1983 and 1997. The data sourceis the Norwegian National Education Database. The database builds ondata from the 1960 and 1970 censuses. Since 1974, data are reporteddirectly to Statistics Norway from the educational institutions.6 To getaccurate measures of time of enrollment, graduation and semestersdelayed, we avoid students that may have been enrolled before 1974,and begin our sample with students who were predicted to graduatein 1983. An individual student's predicted graduation year is his orher year of first entry in higher education plus the length of the educa-tion program the student enrolled in. The largest share of the programswe study lasted for six years, such that a largemajority of those predict-ed to graduate in 1983 first enrolled in 1977. However, some enrolled inlonger programs in 1976 or shorter programs in 1978. As the admissionsystem to higher education changed in 1993, the last students we in-clude in our sample are the predicted 1997-graduates (who enrolled

the form of increased wages and employability (Light, 2001; Ruhm, 1997), and stu-dents may also have preferences for a certain study/work mix which are neglected ina simple pecuniary cost–benefit analysis.

5 This is similar to how a focus on academic performance may erode intrinsic moti-vation for low-ability students and hence be detrimental for their performance (Elliotand Dweck, 1988; Leuven et al., 2010).

6 Our data does not distinguish between private and public institutions. However,during the 1990s, very few people studied graduate degrees at private universities. In-formation about immigrants education from other countries traditionally comes fromdecennial censuses. Non-Western immigrants amount to less than 1% of the sample.

Table 1Distribution of students across the different education programs.

Length of edprogram (years)

No ofstudents

Share(percent)

Treatment group (N = 36,377)Science (cand.scient) 5.5 8736 24.02Humanities (cand.philo) 6 8194 22.53Law (cand.jur) 6 8146 22.39Social sciences (cand.polit) 6 5736 15.77Psychology (cand.psychol) 6.5 1820 5.00Dentistry (cand.odont) 5 1385 3.81Theological seminar (cand.theol) 6 1197 3.29Economics (cand.oecon) 5.5 1081 2.97Arts (music) (cand.musicae) 6 82 0.23

Control group (N = 9989)Medicine (cand.med) 6 4505 45.10Agronomy (cand.agric) 5 3904 39.08Veterinary science (cand.med.vet) 6 617 6.18Pharmaceutical science (cand.pharm) 5 608 6.09Educational science (cand.paed) 6.5 355 3.55

4 T. Gunnes et al. / Labour Economics 25 (2013) 1–11

in 1992 or earlier, most of them in 1991). All variables describing grad-uation year and graduation cohort are based on predicted graduationyear and predicted graduation cohort. For convenience, this is notalways explicitly mentioned in the remainder of the text.

We assign students to the treatment or control group based on thehigher degree program they first enrolled in. This reduces the scope forselection into treatment in response to the reform. However, selectionissues may arise as students that enrolled after the introduction of thereform are included. This will be addressed in Section 5.3. For each stu-dent we have information on whether the student completed a higherdegree or not, and in case of completion, whether it was on time aswell as number of semesters delayed. These variables are calculatedby comparing the stipulated duration of the completed program withthe total time spent studying. Not completed means that we do nothave any record of the student completing a higher degree, at leastnot before 2007 (ten years after stipulated graduation).

Students who are not observed to complete get the value zero onthe on-time completion variable. Furthermore, we truncate numberof semesters delayed at the 5th and 95th percentile. These correspondto −2, i.e., 2 semesters before stipulated completion, and 12 semes-ters, respectively. We have investigated the sensitivity of our resultsto this, finding that different truncation does not give very differentresults.7 However, setting an upper limit to the number of semestersdelayed allows consistent treatment of students who did not completeany higher education. We consider these to be maximum delayed (andimpute using the 95th percentile). Thus, our sample is not affected byendogenous completion.

Although the reform gave an incentive to graduate on time, ourmain outcome variable will be the number of semesters delayed.The average delay for the students in our sample is 5.0 semesters(standard deviation equals 4.7). This variable provides a more preciseindication of the extent to which the reform reduced excess time. Itcaptures the overall change in study behavior, not only whether thestudent succeeds in reducing delay from positive to zero. Also, semes-ters delayed is the most policy-relevant variable as it gives a better in-dication of private and social cost associated with late graduation.8

We also investigate whether more students did graduate on time.This will give us an indication of the share of students who increasedtheir study effort enough to actually get the “bonus”. For completeness,we also check if the reform had an effect on graduating at all. About 75%of the students in our sample did not graduate on time, whereas about19% did not complete their studies at all.

In addition to data on enrollment in, and completion of highereducation, we will also study the effect on labor earnings.9 Earnings isobserved for every calendar year. All earnings are deflated to 1995levels using a wage index. Thus, the population distribution of earningsis approximately stable, and the earnings of an individual reflect hisposition in this distribution. Changes in sample means reflect behavioror career progression. Our main earning measure is earning while study-ing. However, wewill study earnings after graduation as a proxy for skillsacquired in school. Average earningswhile studying is about 52,000 NOKand about 7% of the students have zero earnings at a given time.

We also have background characteristics such as the student's age,gender and parental education and earnings. The data sources for

7 Using the original, untruncated variable (and excluding the non-completers) givesresults similar to our truncated variable. Truncating at the 10/90th percentile, or ex-cluding outliers altogether gives somewhat lower effect estimates, and truncating atthe 1st/99th percentile gives a somewhat higher effect. Results are available uponrequest.

8 While we are able to calculate the cost to treat (see Section 5) , we cannot saymuch about the cost–benefit of the reform, because we do not know the costs and ben-efits of delayed graduation. For instance, the consumption value of attending universityis hard to evaluate.

9 Our earnings measure is earnings that give pension rights, and include wages, busi-ness earnings and certain transfers that replace such income from work (such as sickleave and parental leave), but not e.g. income from capital or earnings-independenttransfers to parents.

parental education and earnings are the same as for the students.We control for the educational level of each parent and for the logof average yearly parental earnings during higher education. Descrip-tive statistics for the outcomes and control variables are given inTable A.1 in Appendix A.

We restrict the sample to students aged 18 to 21 when graduatingfrom high school, who enrolled in a program with a clear treatmentstatus.10 The total number of students in our main analysis sampleis 46,366. Table 1 shows how the students are distributed across thedifferent education programs. The programs affected by the reform(the treatment group) mainly are law, science, humanities and socialsciences. A majority of these programs, apart from law, dentistry andtheology, were non-integrated study programs (i.e., separate under-graduate and graduate degrees), where the last or two last yearswere devoted to writing a master thesis. The programs not affected bythe reform (the control group) consist mainly of integrated five- or sixyear programs, medicine and agronomy being the two most importantones. Amajority of the students in the treatment groupwere enrolled in12-semester programs (i.e., six years), while students in the controlgroup are equally divided across 10 (five years)- and 12-semesterprograms.

Fig. A.1 in Appendix A shows how the number of students enrolledin respectively the treatment group and control group changed overour sample period. During the reform period the treatment group ex-perienced strong growth in enrollment, whereas the control groupwas nearly constant. This is not surprising, given that several of thecontrol programs (notably medicine and veterinary science) are popu-lar with strongly binding constraints for number of students. However,this may raise a concern of whether selection into the treatment pro-grams influences the estimated effect. We investigate this issue furtherin Section 5.3.

In Fig. 1, we show how numbers of semesters delayed changed forstudents with graduation ranging from 1983 to 1997 separately forthe treatment and the control group. During the whole period, thenumber of semesters delayed is lower in the control group than inthe treatment group. Before the reform both groups follow a similar

10 Students completing high school at a higher age, or whose year of high schoolgraduation we do not know constitute about 30% of the student population. Most areelderly people or immigrants, and lack information on date of completion of highschool. Of the remaining students, 44% are excluded. This is mostly because they areregistered with an unspecified program, i.e., we cannot say anything about their re-form status. For some programs the reform status is not clear from the regulations ofthe State educational loan fund. Civil engineering is also excluded. The nominal dura-tion of this degree varied between institutions, which we don't have data about. Fur-thermore, the eligibility for another restitution changed during the reform period forsome civil engineering students, depending on the nominal duration of their program.

Treatment

Control

12

34

56

Num

ber

of s

emes

ters

del

ayed

1980 1985 1990 1995 2000

Predicted graduation year

Fig. 1. Number of semesters delayed, 1983 to 1997.

Table 2Average number of years spent studying under the reform, by year of graduation andtreatment status.

Control group Treatment group Total

1983–1990 0.000 0.000 0.000

5T. Gunnes et al. / Labour Economics 25 (2013) 1–11

pattern. This suggests that absent any reform, the treatment and controlgroups are affected by the same variables, e.g., labor market conditions.

We have also investigated the changes during the reform andpost-reform period more formally by regressing delays on dummiesfor treatment and post-treatment periods. In the treatment groupthe average delay is reduced by about half a semester during the re-form period (estimate is −0.470), and by almost three quarters of asemester in the post-reform period (−0.733). This corresponds to areduction by 0.144 semesters per year treated. In the control group thechanges are of a similar magnitude, but of the opposite sign.11 Withmany potentially confounding variables, it is difficult to credibly estimatean effect from the time-series variation alone. We will therefore formu-late a difference-in-differences model in the next section, comparingchanges in the treatment group with changes in the control group.

As noted above, the degree of exposure to the reform varies con-siderably between students in our sample. Thus, we will allow theeffect of the reform to depend on years studied during the reform,as detailed in the next section. In the remainder of the paper wewill denote year studied during the reform as years treated, for stu-dents both in the treatment and control groups. We measure yearstreated as the number of years a student was in higher educationunder the reform, without having passed her predicted graduationtime. When a student passes the predicted time of graduation, she orhe is delayed, and thus no longer eligible for the restitution. With thetreatment period ranging from 1991 to 1995, the maximum value ofyears treated is five years. In our sample, 19% of the students were en-rolled during the whole reform-period, five years. 18% were enrolledfor four years, whereas 42% had their graduation before the reform(see Appendix Table A.2).

In Table 2 we report the average number of years treated duringthe reform by year of graduation, separately for students in the treat-ment and control groups. Students with graduation in 1990 or earlierdid not have any chance to respond to the reform. Students who grad-uated in 1991 were enrolled one year under the reform, having some

11 An increase of 0.205 semesters during the reform period and 0.692 after, alterna-tively 0.136 semesters per year treated. All estimates are highly significant (at the 5or 1% level). Full results are not reported for brevity, but available upon request. All re-sults are estimated from an individual-level regression. An alternative would be to cal-culate the yearly means of the dependent and control variables and estimate therelationship between these. This gives very similar results, both in terms of magnitudeand significance of the estimates.

opportunity to react, and so on. Because of the short life of the reformrelative to the length of the study programs, the last students to graduateunder the reform would largely have started before its introduction.Furthermore, the first students to graduate after the termination of thereform would mostly have enrolled before or concurrently with theintroduction of the reform. Thus, a majority of these students would betreated during the entire reform, i.e. five years. For each year after thereform ended, graduates' first enrollment will be later, and reform expo-sure less. Our sample ends with the 1997-graduates, who were enrolledfor about four years under the reform. The number of years enrolledunder the reform is somewhat less in the control group, were the pro-grams on average are of somewhat shorter duration.

4. Empirical approach

To estimate the effect of the turbo reform we will rely on thefollowing difference-in-differences framework. Di is a dummy variablethat equals one if student i enrolled in the treated programs and zeroif he/she belongs to the control group:

yit ¼ α þ ϕDi þ dt þ ηTTit þ γ1 Di⋅T

Tit

� �þ γ2 Di⋅d

Tt

� �þ γ3 Di⋅d

PTt

� �

þ βXi þ εit: ð1Þ

The outcome variable yit measures how many semesters student iwith predicted graduation in year t is delayed. TitT is years treated, asdiscussed in the previous section. dt is a set of dummy variables for

1991 1.000 1.000 1.0001992 2.000 2.000 2.0001993 3.000 3.000 3.0001994 4.000 4.000 4.0001995 5.000 5.000 5.0001996 4.542 4.972 4.9021997 3.587 4.026 3.941Total 1.713 2.218 2.109

6 T. Gunnes et al. / Labour Economics 25 (2013) 1–11

predicted graduation year, dtT is a dummy variable equal to one if thepredicted graduation year is during the reform period (1991–1995),dtPT is a dummy variable equal to one if the predicted graduation year

is after the reform period (1996–1997). Xi is a vector of covariates(including dummy variables for age, gender, length of the studyprogram and parental education and earnings, and described morein Section 3), and �it is a random error term.

Our parameters of interest are the difference-in-differences pa-rameters γ1, γ2 and γ3. γ1 measures the reform effect for each yeartreated, and is expected to be negative (less delay with more treat-ment). γ2 and γ3 capture that the effect of the reformmay not be pro-portional with time treated. That is, to allow for more general effects,we add interaction terms between the dummy variable for being inthe treatment group and the dummy variables for whether thestudent's predicted graduation year was during or right after the re-form period. Hence, the respective reform effects for students with pre-dicted graduation during and after the reformperiod becomeγ1Tit

T + γ2

and γ1TitT + γ3. Conditional on the effect of years treated (γ1), γ2 and γ3

capture, among other things, the potential effect timing of the incentivemay have on semesters delayed. If being treated late in the study pro-gression ismore important than being treated early (e.g. because delaystend to arise in the last part of a degree), the effect of the incentiveshould be larger for students graduating during the reform-periodthan for students graduating after the reform-period, γ2 b γ3

(i.e., more of a reduction in delay for those graduating during the re-form period). Likewise, if the opposite is the case (e.g. because ofhabit formation in early studying years), γ3 b γ2. Furthermore, γ3 b γ2

could also reflect a change in study norms where there is a persistentreform effect, e.g. because excess time is less accepted among peers orpotential employers. While the estimated values may give indicationsof which of the above stories are the more relevant ones, we cannotwith any degree of certainty distinguish between potential mecha-nisms. In particular, as we do not have any post-reform students thatare not treated to a large degree in our sample, it is hard to judge ifthere is any persistent effect for non-treated students.

As previous research has found different effects for high and lowability students (Leuven et al., 2010), we also estimate models wherewe interact years treated with a dummy variable for whether at leastone of the parents have a higher degree (corresponding to 15+ yearsof schooling, the dummyvariable is denotedHi). Furthermore, the effectof the reform may also vary with parental earnings. The incentive maybe weaker for students with higher-earning parents if they to a larger

Table 3The effect of financial incentives on semesters delayed.

(1) (2)

Treatment 3.698 (0.073)*** 3.667 (0.Treatment ∗ reform years (γ2) −0.812 (0.106)***Treatment ∗ post reform years (γ3) −1.524 (0.136)***Years treated −0.337 (0.Treatment ∗ years treated (γ1) −0.277 (0.MaleMother's ed (ref = ≤compulsory)– Intermediate– TertiaryFather's ed (ref = ≤compulsory)– Intermediate– TertiaryLog of parents' earningsMissing parental earningsYears treated ∗ parents tertiary ∗ treatmentYears treated ∗ log parents' earn ∗ treatmentR-squared 0.125 0.125Nr. of observations 46,366 46,366

Note: Included in all specifications are year dummies for predicted graduation year and for ldummies for missing information on parental education and dummies for age when graduavariables belonging to the treatment group and years treated with parents' tertiary educatisignificant at the 10/5/1% level.

degree can rely on inheritance or transfers from their parents. On theother hand, if the parents can support them financially, they may alsohave more opportunity to not work while studying, and to increaseprogression in response to the reform. For this reason, we also interactthe years treated with log of parents' total earnings (Ei).

Thus, the estimated reformeffect for a student predicted to graduatein the reformperiod is (γ1 + γ1

H ⋅ Hi + γ1E ⋅ Ei) ⋅ TitT + γ2 (similarwith

γ3 replacing γ2 for a student with predicted graduation after the re-form), i.e., it is allowed to vary with parental education and earnings.Earnings are measured as deviations from the sample average, suchthat γ1 captures the effect per year treated on a student with averageparental earnings. Note that we let the dependency of the reform effecton graduation during/after the reform period be the same, irrespectiveof parental education and earnings.

With difference-in-differences studies there is always a concernthat the estimates are affected by differential trends or shocks. Tocheck the robustness of the reform effects, we investigate the trends instudy duration by estimating a more general difference-in-differencesequation than Eq. (1) containing year-specific effects (so-called placebo“reform” effects). In this specification, we estimate year-specific parame-ters that measure the difference between the treatment and controlgroup, relative to the difference in 1989 (i.e., just before the reform). InSection 5.3 we discuss further sensitivity checks.

5. Results

This section presents the estimates of the effects of the reform.Westart out by looking at the effect on our main variable, semestersdelayed, as well as two closely related variables: On-time graduationand non-completion (Section 5.1). In Section 5.2 we investigate theeffect on the students' earnings, whereas several robustness checksare conducted in Section 5.3.

5.1. Effect on delay and graduation

Columns (1)–(4) in Table 3 report different variations of Eq. (1). Inthe first column we disregard years treated and only estimate theeffect of graduating during or right after the reform-period, i.e. γ2 andγ3. On average, delays were reduced by 0.81 semesters during the re-form period, and by 1.52 semesters in the first two post-reform years.Both effects are statistically significant at the 1% level. Modeling thereform effect as proportional to years treated, γ1 (column (2)), each

(3) (4) (5)

070)*** 3.679 (0.074)*** 3.567 (0.074)*** 3.575 (0.074)***−0.097 (0.202) −0.060 (0.201) −0.059 (0.201)−0.388 (0.279) −0.331 (0.278) −0.323 (0.278)

156)** −0.254 (0.162) −0.282 (0.160)* −0.245 (0.163)024)*** −0.229 (0.055)*** −0.223 (0.055)*** −0.226 (0.061)***

−0.549 (0.042)*** −0.547 (0.042)***

−0.280 (0.064)*** −0.294 (0.064)***−0.263 (0.074)*** −0.292 (0.084)***

−0.194 (0.075)*** −0.199 (0.075)***−0.310 (0.080)*** −0.369 (0.109)***−0.380 (0.055)*** −0.339 (0.077)***−0.117 (0.086) −0.105 (0.088)

0.074 (0.055)0.105 (0.055)*

0.125 0.134 0.13546,366 46,366 46,366

ength of education program and a constant term. Specifications (4) and (5) also includeting from high school. Specification (5) also controls for the interactions of each of theon and log earnings. Standard errors are heteroskedasticity robust. */**/*** statistically

13 The slow response may have other explanations, for example information spread-ing or peer effects. Information spread is unlikely to be important, given that studentsget detailed information from the State educational loan fund (cf. Section 2.2). Peer ef-

7T. Gunnes et al. / Labour Economics 25 (2013) 1–11

year of treatment reduces delay by 0.28 semesters. This effect is alsostatistically significant at the 1% level, and amounts to 1.4 semestersfor a student who is treated during the entire duration of the reform(0.28 ∗ 5 years). The baseline difference between the treatment andcontrol groups is as high as 3.7 semesters, thus, even though the reformeffect is substantial, it far from eliminates the difference between thegroups.

The more flexible specification in column (3) (including γ1, γ2 andγ3) reduces the effect of each year treated marginally to 0.23. On theother hand, both γ2 and γ3 are reduced substantially compared tocolumn (1). This suggests that the reform effect mostly depends onthe amount of time treated, rather than the timing of the incentive,i.e. whether a student graduated during the reform or after the reformended. However, γ2 and γ3 contribute to a larger reform effect, asthey are still negative, if not significant. Although γ2 and γ3 are notsignificantly different, the larger absolute value of γ3 may suggestthat early treatment is important. There seems to be a higher effectfor students treated early in their studies than for students treatedfor a similar period towards the end of their education. These resultsmay then indicate that the reform is most effective for students treatedearly in their education. However, although the effect for students treatedlater in their education is somewhat smaller (for similar length oftreatment), delays are significantly reduced also for these.

Controlling for gender and background variables in column (4) doesnot change the difference-in-differences estimatesmuch. This indicatesthat changes in the composition of the treatment and control groups interms of individual characteristics do not contribute to our estimatedreform effects. Moreover, it suggests that selection on students' familybackground is not important, which is reassuring as no prior achieve-mentmeasure is available. As for the estimated coefficients on the back-ground variables, male students and students of higher-educatedparents are on average less delayed than female students and studentswhose parents have shorter education. The opposite seems to be thecase for students with higher parental earnings.

Column (5) presents resultswherewe interact number of years treat-ed with parental education and earnings. There are no indications thatthe reform effect differs across students with different parental educa-tion. On the other hand, there is a significant difference in reform effectby earnings, if only at the 10% level. However, the difference in reformef-fect is rather small. Ten percent higher parental earnings correspondsonly to about 0.01 fewer semesters delayed for each year treated.

To investigate the relationship between financial incentives andstudy duration further, we also look at other outcome variables thanthe number of semesters delayed. The results are reported in Table 4.Apart from the dependent variable, the models presented are equiva-lent to the model in column (4) of Table 3.12

As the restitution was given to students who completed theirstudies on time we start out by regressing the reform effects on adummy variable indicating whether the student has graduated ontime or not, see column (1). The share of students graduating ontime increases by about 3.8 percentage points for each year treated,from a baseline probability of about 20%. However, this is partly offsetby a negative constant term, such that for students treated for four orfive years, the probability of on-time graduation increases by 8–11percentage points (see upper panel). This can also be seen from theestimates from a simpler model, where we omit the reform periodand post reform period indicators, i.e., set γ2 = γ3 = 0 (see lowerpanel). Even though the reform was not meant to have an impactgraduating per se, we cannot rule out that this was the case. Somemarginal students may be induced to continue in order to get the res-titution. In column (2) the dependent variable is a dummy whichequals one if the student did not complete. All the reform effects aresmall and statistically insignificant, suggesting that the reform did

12 These models are estimated with a linear probability model, using a logit modeldoes not change our conclusions.

not influence graduation. However, all the estimates are also negative,and forcing the effect to be proportional to years treated, we do get asignificantly negative result. Thus, it does seem that the reform hadsome effect on completion. However, when excluding students thatdid not complete their studies (column (3)), the reform effect on com-pleting on time is basically unaltered. The reform effect seemsmostly tobe driven by students that would have graduated anyway.

From the estimates in Tables 3 and 4 it is possible to do someback-of-the-envelope calculations of the cost to treat of the reform.With three years of treatment, which about corresponds to the aver-age for those treated, we get an estimated effect of a reduction ofdelays by about 0.8 semesters for those graduating during the reform(γ̂1⋅3þ γ̂2 ¼ −0:79, using column (3) from Table 3). Furthermore,this means an about 4 percentage point increase in the share graduat-ing on time (γ̂1⋅3þ γ̂2 ¼ −0:036, using column (1) from Table 4). Ifwe extrapolate the effect of the reform to six years of treatment (theduration of the most treated program) – this is an out-of-sample pre-diction, and should be interpreted with caution – the correspondingeffects are about 1.5 semesters less delay and 16 percentage pointsmore on time. Thus, with three years of treatment, for each six resti-tutions given, in about one case the student graduates on time be-cause of the reform. With six years of treatment, the correspondingfigure is one for every 1.8 restitutions given.

The year-specific difference-in-differences estimates for all threeoutcome variables (number of semesters delayed, graduating ontime, and not completing) are reported in Table 5. First, in column(1),we notice that there are no indications of (placebo) “reform effects”on the number of semesters delayed before the implementation of thereform. The sign of the estimated coefficients vary, and none are statis-tically significant. This is noteworthy, as it statistically confirms our im-pression that the trends in Fig. 1 are parallel, and indicates that ouridentifying assumption is indeed justified. We do find two significantpre-reform “effects” for the other two outcomes in columns (2) and(3) (one of these, only at the 10% level). However, testing a largenumber of coefficients, it is not surprising that some are significant. Fur-thermore, even the significant pre-reform estimates are small, and thepre-reform estimates show no obvious pattern or other indication ofdifferential pre-reform trends.

There are no significant reform effects in the three first years ofthe reform, but consistent positive effects (i.e., reduced delay,increased share on-time and fewer non-completers) in the subse-quent years. While the reform effect does not increase linearly, theyear-specific estimates are not very precise, thus we cannot rulethis out. Taken at face value, the estimates suggest a slow but lastingimpact of the reform. This result may imply that it is particularly im-portant that treatment starts early and hence complements previousfindings that γ3 b γ2 b 0. The students affected seem to be those withabout two or more years left of their studies at the introduction of thereform. Recall that for most of the treatment programs, the last twoyears constitute a graduate degree, a large part of which was towrite a thesis. Our year-specific results seem to indicate that it is im-portant that students are exposed to the incentive at the latest whenstarting this part of their studies.13 Regarding non-completion(column (3)), we find an effect on the share completing highereducation for the later years. This is in linewith the simple specificationin column (2) Table 4. However, this effect is too small to explain the in-crease in on time graduation in column (2).

fects could matter e.g. if students initially consider the restitution out of reach, but seethat other students get it. This should give a more gradual increase in the reform effectthan what we observe in Table 5. However, as noted in the text, the estimates are tooimprecise to rule out such a gradual increase.

16 Furthermore, dentistry students face strict admission requirements. While therewere no strict admission requirements in law, there was a cut-off after two years such

Table 4The effect of financial incentives on completing on time and completing at all.

Dependent variable (1) (2) (3)

On-time graduation Not completed On-time graduation

Upper panelTreatment −0.235 (0.008)*** 0.135 (0.006)*** −0.225 (0.009)***Treatment ∗ reform years (γ2) −0.067 (0.021)*** −0.009 (0.016) −0.083 (0.022)***Treatment ∗ post reform years (γ3) −0.078 (0.029)*** −0.026 (0.022) −0.102 (0.031)***Treatment ∗ years treated (γ1) 0.038 (0.006)*** −0.007 (0.004) 0.040 (0.006)***

Lower panelSpecification with γ2 = γ3 = 0: 0.022 (0.003)*** −0.010 (0.002)*** 0.020 (0.003)***Treatment ∗ years treated (γ1)Included in sample All students All students Students graduatedR-squared 0.201 0.024 0.231Nr. of observations 46,366 46,366 37,627

Note: In total, six models are estimated; three models in the upper panel, and three in the lower panel. R-squared is the same for both models presented in the same column. Incolumn (1) we impute those not graduated as delayed. In column (3) we exclude students that did not complete their studies. Included in all specifications are dummies for pre-dicted graduation year, dummies for length of education program, students' background characteristics and gender and a constant term. Standard errors are heteroskedasticity ro-bust. */**/*** statistically significant at the 10/5/1% level.

8 T. Gunnes et al. / Labour Economics 25 (2013) 1–11

5.2. Effects on earnings

In Table 6 we present the estimated effect of the reform on (thelogarithm of) earnings while studying. In line with our generaldifference-in-differences approach, the effect is estimated as an inter-action between treatment group and reform period. Note however,that here the reform period variable does not relate to graduationyear, but rather the year of the earnings observation. Thus, we esti-mate the reform effect by comparing the earnings in the reformyears for treatment and control students that have not passed theirpredicted graduation dates. As the aim is to study earnings whilestudying, and not pick up transitions between work and study, westart our sample with the first year after the first enrollment in highereducation, and only include years before the predicted graduationyear.14 In all specifications, we control for time-invariant differencesbetween the treatment and control groups, as well as for year effectscapturing shared variation over time.

Column (1) in Table 6 shows that the students in the treatmentgroup tend to earn just over 15% more than the students in the controlgroup. During the reform years, this difference is reduced by about 5percentage points. This effect is significant at the 1% level. Furtheradding program-specific constant terms and trends, capturing differencesin earning opportunities between students of different programs (column(2)) gives a reform effect of about 4%, significant at the 5% level. Finally,including student fixed effects in column (3) gives a reform effect ofjust over 3%. This is only significant at the 10% level. However, the estimat-ed reform effect is relatively stable across the different specifications.

The results suggest that students in the treatment group, in re-sponse to the reform, reduce their earnings by about 3–4% relativeto the control group. Average earnings among the eligible studentsare about 60,000 NOK (deflated to the 1995 wage level), such thatthis effect corresponds to about 2000 NOK in each year of treat-ment.15 The fact that students seem to shorten their study durationby working less while studying support the hypothesis mentionedin Section 2.4, that a positive reform effect may work, at least inpart, through other mechanisms than increased study effort. The re-form seems to cause a certain loss of value added from students, how-ever, this cost is small. Longer-term earnings may give an indicationof whether or to what extent the reform affects the quality of andsubsequent returns to the students' investment in education. Estimat-ing reform effects on earnings from one to ten years after stipulated

14 This also means that we exclude students that are no longer treated because theyhave passed their nominal graduation.15 As we study log earnings, all individuals with zero earnings (about 7% of the sample)will be excluded. However, we find no reform effect on the share with zero earnings. Es-timates are insignificant and very close to zero. Results are available upon request.

graduation, we find no clear effects (results available upon request).Thus, there do not seem to be changes in human capital acquisitionthat contribute to the costs or benefits of the reform. These resultsalign with Humlum and Vejlin (2011), who find that increased trans-fers among high-school students decreases part-time work, but haveno effect on academic performance.

5.3. Sensitivity checks

In this section we conduct several robustness checks in order toinvestigate the sensitivity of our findings. In each case the evidencesupports that our estimates capture a genuine reform effect. We re-port some key sensitivity checks in Table A.3, detailed results fromother checks are available upon request.

First, in column (1) in Table A.3 we restrict the treatment group tothe integrated programs dentistry, law and theology, which have astructure and teaching similar to that of the control group, the estimatedreform effect is somewhat reduced, but there is still a significant reduc-tion of delays with more years treated.16 Likewise, restricting the treat-ment and control group to programs of similar duration also gives asignificant reform effect.

Second, as the reform may influence enrollment into treatmentand control programs differently (recall Fig. A.1), in column (2) weexclude students who enrolled after the introduction of the reform.We find an effect that is stronger than the one in Table 3. Thus, selec-tion into treatment programs cannot be ruled out. However, selectionseems to contribute to increased delays, which is consistent with themarginal students having a higher expected delay.

Third, we estimate the reform effects for students with graduationwithin three years of the introduction of the reform (the 1988 to 1993graduation cohorts, reported in column (3)). This reduces the scopefor omitted differential trends, and produces an estimated reform ef-fect slightly larger than the one in the main specification.

Finally, controlling for a range of other potentially confoundingvariables, such as program-specific effects and linear trends, (the log-arithm of the) treatment/control specific cohort sizes and labor mar-ket conditions, does not affect the results much.17

that students needed a grade of B or better on their two-year exam to continue.17 We capture labor market conditions with program-specific earnings and earningsgrowth and treatment/control-specific effects of the national unemployment rate.The period under investigation started with a quite strong recession but the economystarted to boom around 1993, e.g. Hakkinen and Uusitalo (2003) suggest that this mayhave differential impacts on delays.

Table 6Effects on log earnings while studying.

(1) (2) (3)

Treatment 0.150 (0.018)***Treatment ∗ reform years −0.054 (0.020)*** −0.040 (0.020)** −0.032 (0.018)*Years to pred. grad −0.110 (0.002)*** −0.121 (0.002)*** −0.233 (0.031)***Control ∗ unemployment 0.001 (0.007)Program-fixed effects and trends No Yes YesIndividual fixed effects No No YesR-squared 0.034 0.058 0.040Nr. of observations 207,205 207,205 207,205

Note: Included in all specifications are dummies for gender and year of observation. Standard errors are heteroskedasticity robust. */**/*** statistically significant at the 10/5/1% level.

Table 5Year specific difference-in-differences estimates (placebo testing).

Dependent variable (1) (2) (3)

Nr of sem delayed On-time graduation Not completed

Treatment 3.676 (0.183)*** −0.264 (0.020)*** 0.141 (0.014)***Treatment ∗ year (ref = 1989)– 1983 0.078 (0.258) 0.066 (0.028)** 0.026 (0.021)– 1984 0.120 (0.260) 0.015 (0.028) 0.024 (0.021)– 1985 −0.325 (0.273) 0.032 (0.028) −0.025 (0.022)– 1986 −0.270 (0.269) 0.009 (0.028) −0.037 (0.022)*– 1987 0.019 (0.259) 0.025 (0.028) −0.004 (0.020)– 1988 −0.106 (0.266) 0.021 (0.028) −0.006 (0.021)– 1990 −0.216 (0.262) 0.032 (0.028) −0.030 (0.020)– 1991 −0.262 (0.265) −0.008 (0.028) −0.019 (0.021)– 1992 −0.065 (0.256) −0.011 (0.027) 0.004 (0.020)– 1993 −1.191 (0.262)*** 0.105 (0.028)*** −0.061 (0.021)***– 1994 −1.065 (0.246)*** 0.118 (0.026)*** −0.043 (0.019)**– 1995 −1.409 (0.252)*** 0.146 (0.027)*** −0.055 (0.020)***– 1996 −1.450 (0.250)*** 0.121 (0.027)*** −0.051 (0.020)***– 1997 −1.619 (0.243)*** 0.158 (0.026)*** −0.067 (0.019)***R-squared 0.135 0.201 0.024Nr. of observations 46,366 46,366 46,366

Note: Included in all specifications are year dummies for predicted graduation year, dummies for length of education program, students' background characteristics and gender anda constant term. Standard errors are heteroskedasticity robust. */**/*** statistically significant at the 10/5/1% level.

Treatment

Control

500

1000

3000

Stu

dent

s en

rolle

d (lo

g sc

ale)

1980 1985 1990 1995 2000

Predicted graduation year

Fig. A.1. Number of students enrolled, 1983 to 1997.

Appendix A

9T. Gunnes et al. / Labour Economics 25 (2013) 1–11

Table A.2Average number of years enrolled under the reform, by treatment status.

Control group Treatment group Total

Nr Percent Nr Percent Nr Percent

0 4960 49.65 14,635 40.23 19,595 42.261 613 6.14 2151 5.91 2764 5.962 643 6.44 2422 6.66 3065 6.613 1081 10.82 2715 7.46 3796 8.194 1492 14.94 6728 18.50 8220 17.735 1200 12.01 7726 21.24 8926 19.25Total 9989 100 36,377 100 46,366 100

Table A.3The effect of financial incentives on graduating on time different samples, estimated by OL

(1)

Upper panelTreatment 2.076 (0.087)***Treatment ∗ reform years (γ2) 0.100 (0.251)Treatment ∗ post years (γ3) −0.096 (0.330)Treatment ∗ years treated (γ1) −0.125 (0.067)*

Lower panelSpecification with γ2 = γ3 = 0:Treatment ∗ years treated (γ1)

−0.122 (0.029)***

Sample Integrated programsR-squared 0.102Nr. of observations 18,135

Note: In total, six models are estimated; three models in the upper panel, and three in thecluded in all specifications are dummies for predicted graduation year, dummies for lengthterm. Standard errors are heteroskedasticity robust. */**/*** statistically significant at the 1

Table A.1Descriptive statistics for the estimation sample (fractions unless otherwise noted).

Outcome variables

Nr of semesters delayed 4.981Students graduating on time 0.248Students not completing 0.188Average earningsa while studying 52

Explanatory variables

Years treated 2.109Average length of study programs 11.5Male 0.498Average age end of high school 19.12Mother's education– Compulsory (0–10) 0.156– Intermediate (11–14 years) 0.495– Tertiary (15–20+) 0.323– Missing 0.026Father's education– Compulsory (0–10) 0.108– Intermediate (11–14 years) 0.396– Tertiary (15–20+) 0.457– Missing 0.039Average of parents' earnings 440Missing parental earnings 0.108

a All earnings expressed in 1000 NOK, deflated to 1995 levels with a wage index. Ourmeasure of parental earnings is the average of the sum of the parents' earning, over theyear of predicted graduation and the five preceding years. As earnings are deflated, theearnings measure reflects the parents' position in the earnings distribution, rather than(real) purchasing power. In the analyses, we control for missing information on paren-tal with a dummy.

10 T. Gunnes et al. / Labour Economics 25 (2013) 1–11

6. Conclusion

Ensuring access and equal opportunity in higher education is a cen-tral aim of policy makers. A pivotal policy instrument in this regard isstate-provided grants and favorable students' loans. However, subsidiz-ing time spent studying in order to increase students' level of attain-ment may have undesired consequences in the form of reduced studyefficiency because the support reduces the marginal cost of studying.

In this paper we study the effects of financial incentives on studyduration. We investigate the effect of a reform that rewarded stu-dents who completed their higher education degree on nominaltime, using rich register data in a difference-in-differences frame-work. We find that the share of on-time graduation increases by 3.8percentage points per year treated, from a pre-reform level of about20%. Thus, a large share of the restitution given will be for studentswho would otherwise not have graduated on time. Moreover, inorder to capture to overall effect of the reform, we find that the aver-age delay in the treatment group decreased by 0.8 semesters duringthe reform period, and by 1.5 semesters in the following two years.The large effect in the first post-reform years points to a strong effectof the duration of the treatment, we find that delays are reduced by0.23 semesters per year treated. Furthermore, there is some indica-tion that it is important that treatment starts before the final part ofthe educational programs, potentially indicating that early treatmentis important to establish efficient study habits. A series of robustnesschecks indicate that our estimated effects do not reflect differentialtrends or omitted variables.

Because few students initially graduated on time, the cost to treatis low. Furthermore, there is little indication of adverse effects. Wefind no indication that students that are unable to get a restitutionare discouraged and perform worse. Students reduce their earningswhile studying, suggesting less work and more time allocated tostudying. However, the change in earnings is small, suggesting thatthe main response and cause of the reduction in delays is to increasestudy effort. Finally, there are no effects on earnings after graduation,neither in the short nor longer run.

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