Does enhanced mobility of young people improve employment and housing outcomes? Evidence from a large and controlled experiment in France

Journal of Urban Economics 97 (2017) 1–14

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Journal of Urban Economics journal homepage: www.elsevier.com/locate/jue

Does enhanced mobility of young people improve employment and housing outcomes? Evidence from a large and controlled experiment in France Julie Le Gallo a,∗, Yannick L’Horty b,1, Pascale Petit b,1 a b

CESAER, AgroSup Dijon, INRA, Univ. Bourgogne Franche-Comté, 26 Boulevard Petitjean, F-21000 Dijon, France ERUDITE, Université Paris-Est Marne-La-Vallée, 5 bd. Descartes - Champs/Marne, 75454 Marne- La-Vallée, France

a r t i c l e

i n f o

Article history: Received 23 July 2015 Revised 29 September 2016 Available online 19 November 2016 JEL classification: H22 J64 L38 C93 Keywords: Randomised controlled trials Drivers‘ license Mobility Employment

a b s t r a c t For disadvantaged young people, access to a means of transportation, whether in the form of a personal vehicle or reliable public transportation, can play an important role in determining school-to-work transitions. In order to find a clean source of identification to assess the impact of reducing commuting costs for such individuals, we conducted a large and controlled experiment to study the impact of the intervention of subsidizing driving lessons in France by randomly assigning young candidates to one of two groups made up of treated and untreated individuals. We assessed the impact of improving their degree of mobility through this intervention on several outcomes, including drivers’ testing results, housing, and employment status. We found that young people are less mobile during their training period, and therefore less involved in actively seeking employment or improving on their current position. Once they have passed the driving test, however, these findings are reversed. Finally, we do not discern any significant impact on the important outcome of access to permanent jobs, but we do find a positive yet weak effect on access to temporary jobs. © 2016 Elsevier Inc. All rights reserved.

1. Introduction Does enhanced geographic mobility improve employment outcomes? For those who suffer most from a lack of mobility, including young people without a driver’s license and/or with little access to either personal or public transportation, the answer will probably always be affirmative. The day-to-day difficulty they experience when commuting independently undoubtedly plays a major role in determining their school-to-work transition. It impacts access to professional training as well as access to employment. From the employer’s point of view, low mobility leads to a higher risk of tardiness or absenteeism, as well as to a lower degree of flexibility in the young person’s work scheduling (van Ommeren et al., 2011). From the perspective of a young person seeking employment, low mobility leads to a longer and costlier employment search (Rogers, 1997; Immergluk 1998; Wasmer and Zenou, 2006). This proposition was confirmed by several empirical studies that emphasize how the most vulnerable groups in the labor mar-

∗

Corresponding author. Fax. +33 3 80 77 25 00. E-mail addresses: [email protected] (J. Le Gallo), [email protected] (Y. L’Horty), [email protected] (P. Petit). 1 Fax. +33(1)60 95 70 60. http://dx.doi.org/10.1016/j.jue.2016.10.003 0094-1190/© 2016 Elsevier Inc. All rights reserved.

ket are also penalized by the high cost of public and private transportation. Access to a car can increases the chances of being employed and influences the quality of employment, as measured by the number of hours worked or by the pay level (Raphael and Rice, 2002; Gurley and Bruce, 2005). This seems especially true for those who face the highest obstacles to gaining employment, particularly minimum-income recipients (Ong 2002; Blumenberg and Hess, 2003). Conversely, a lack of access to public transportation or to private vehicles further undermines labor market opportunities, especially for those living in the most deprived neighbourhoods (Kawabata, 2003; Ong and Miller, 2005). From an empirical point of view, the task of assessing the impact of daily mobility on employment-related outcomes is hampered by an endogeneity problem. The difficulty lies in evaluating whether young people lack employment due to their low mobility, or whether their lack of mobility is caused by their unemployment (or jobless) status. To assess causality in spatial contexts such as this one, most authors have adopted an instrumental variable strategy. For instance, Ong (2002) and Raphael and Rice (2002) use state-level variations in gasoline taxes and insurance premiums as instruments. Alternatively, Baum (2009) uses state regulations (regarding asset possession) specifying welfare eligibility as instruments.

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This paper uses a direct and clean source of identification regarding the empirical impact of reducing commuting costs for individuals. Indeed, it involves a large and controlled experiment to evaluate the impact of lower driving lesson costs in France by randomly assigning young candidates to one of two groups comprised of treated and untreated individuals. This experiment allows us to measure the causal impact of reduced commuting costs on employment status as well on housing status (e.g. whether or not the young person lives independently). The experiment entitled “Dix mille permis pour réussir” (Ten Thousand Licenses for Success) involved the distribution of 10,0 0 0 vouchers in the amount of €10 0 0 for each young person, most of whom were NEET (Not in Education, Employment or Training) individuals. Since obtaining a driver’s license requires expensive instruction that can last for over a year and involves a minimum investment of approximately €1500, this voucher led to a proportional cost reduction of up to two-thirds. In our experimental analysis, individuals in the “test group” were awarded the voucher to pay for their driving lessons and received support from a social center1 throughout these lessons. Individuals in the “control group” received the standard welfare benefits for the underprivileged. We evaluated the impact of the voucher mechanism by comparing the outcomes for the test and control groups using two surveys, conducted one and two years after the respondents joined the experiment, while controlling for contextual and local data. The evaluation covers a sample of 154 non-profit organizations throughout France, mostly involving the missions locales that support approximately 60 0 0 young people by providing financial assistance to help defray the cost of the driving tests, which were held between January of 2010 and June of 2012. This paper is thus in line with the growing literature involving randomized experiments applied to evaluate the efficacy of public policies (Miguel and Kremer, 2004; Banerjee and Duflo, 2009). In assessing the impact of the reduction in commuting costs occasioned by the subsidized driving lessons, we randomized selection across people rather than locations. There are a few examples of randomized trials involving transportation subsidies in developing countries (Bryan et al., 2014; Franklin, 2015). To the best of our knowledge, however, the only existing paper that has taken an experimental approach in the policy area of driver’s licenses is Bertrand et al., (2007), which analyzed the effect of corruption in India by monitoring 822 driving test candidates. Although such experiments have recently been developed in France for employment searches (e.g. Crépon et al., 2013), they remain rare in the literature, especially for interventions on a scale equal to the “Dix mille permis pour réussir” program. A scale of such considerable size encompasses a wide variety of local economic and social contexts, which reinforces the external validity of our results. In addition, only one paper has dealt with the employment impact of a driver’s license in France (Avrillier et al., 2010). Those authors used the event of the abolition of mandatory national military service as a natural experiment to assess the supply and demand effects in the market for drivers’ licenses. We investigated three types of outcomes, including driving, housing, and employment status. Our results show that the experiment was clearly beneficial at each step of the drivers’ education process. The difference between treated and untreated individuals is about 20% points when taking the theoretical portion of the test, a figure that remains stable in both surveys (respectively 53% and 66% for the test group, 34.2% and 47.2% for the control group). The estimated impacts tend to be higher for results derived from 1 There are specialized social centers for young people aged 16 to 25 years in France, called missions locales. They do not give stipends to the young but rather accompany them in their social and professional integration by providing advice and ad hoc support.

the second survey. For instance, the discrepancy between the two groups on the practical portion of the test is approximately 0.11 for the first survey and 0.14 for the second survey. The differences for the outcome of car ownership are 0.06 for the first survey and 0.15 for the second survey. We also show that the impact of the treatment is particularly beneficial for individuals with at least an upper-secondary education level. The effect was positive for those living in independent housing one year after the test occurred, but slightly negative after two years. With respect to the outcome of any move to a new location, the effect is significant and negative in both years, although this impact is higher in absolute value for the first year. This highlights the program’s lock-in effect; young people must stay at the same location throughout the learning period in order to benefit from the subsidies and non-monetary support. This limits their residential mobility for a certain period. We also found that young people were less likely to actively seek employment, or to improve their current employment situation, during their training period. Once they passed the test, however, these outcomes were reversed, and young people were able to find work more easily. The impact of owning the driver’s license on employment only appears two years after the experiment, and it is not significant for the event of obtaining a permanent job. It is significant only for the event of obtaining a temporary job. From the perspective of public policy, grants promoting the mobility of people provide an alternative to location-based policies. Moreover, these grants avoid the adverse effects of location-based subsidies, which encourage the displacement of activities and people without necessarily improving employment outcomes for local workers and firms. These effects are especially important when the degree of mobility of people is high (Kline, 2010). In either case, it is appropriate to consider the general equilibrium effects before recommending any generalization for this type of intervention. This is why we have inserted controls in our estimating equations for possible spillover effects among treated and untreated young people using the method set out by Baird et al., (2014). Our results highlight the presence of a congestion effect; as the number of examiners is limited locally, there is a negative spillover of untreated young people in the area. Finally, we do not recommend generalizing this type of assistance given the magnitude of the lock-in effects when obtaining a driver’s licenses as well as the weakness of the estimated employment effects. It would be more cost efficient to simplify the driving test in order to increase the mobility of young people and to facilitate their employment search. The paper proceeds as follows. Section 2 sets out the design of the experiment and describes how the data were collected. Section 3 presents the findings. Section 4 concludes. 2. The experiment The “Dix mille permis pour réussir” experiment was launched in 2010 by the French Ministry of Youth, under the auspices of the Fonds d’Expérimentation pour la Jeunesse.2 A national call for tenders was issued to all neighbourhood offices for the social and professional integration of young people (commonly referred to as missions locales). These non-profit organizations selected young people with integration difficulties, low educational achievement and very little work experience in an effort to help them learn to drive. Young people wanted to obtain their driver’s license and volunteered to participate in the experiment.

2 Created in late 2008, the Fonds d’Expérimentation pour la Jeunesse (FEJ) is an innovation in the French institutional landscape. It combines contributions from both state and private partners to fund experimental mechanisms for young people. Initially focused on social and occupational integration, the fund was incorporated into the Ministry of Education in 2010 and currently covers all school policies that impact young people under the age of 25.

J. Le Gallo et al. / Journal of Urban Economics 97 (2017) 1–14

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Fig. 1. Calendar of the experiment.

The experiment involved the distribution of 10,0 0 0 vouchers in the amount of €10 0 0 to help each young person pay for their driving lessons. This amount is slightly less than the net minimum wage per month and covers two-thirds of the average cost of a driver’s license in France (see Appendix A for more information on the French driver’s license). Young people also received support from a welfare center throughout their driving instruction. The quantitative evaluation covered only the 30 largest non-profit organizations grouping 154 different centers. Each center supported 8 to 150 young people. In total, 60 0 0 young people received support from the 30 large non-profit organizations and were included in the evaluation protocol. The young people were identified individually by their case worker, often a social worker in a mission locale, who completed a single form using an extranet site specifically designed for the experiment. The potential beneficiaries filled out the form to register their social and occupational status. The forms were centralized and statistically processed to analyze the profiles for each candidate. Young people were assigned to either the control group or the test group based on a random draw: three out of four young people were awarded the subsidy. These three in four beneficiaries formed the test group and were given the voucher. The remaining one in four non-beneficiaries formed the control group and received the usual access to local assistance (see Appendix A). Note that we did not have any compliance problems in the experiment, since nobody refused this voucher after having been randomly assigned to the treatment group. We then evaluated the impact of the voucher mechanism by comparing the test and control groups through two surveys conducted one and two years after the respondents joined the experiment (Fig. 1). The first survey was conducted between April and May of 2011, while the second was conducted during the same period 12 months later. Each survey covered 1800 young people. Upon their enrolment, every young person was informed that their subsidy was not guaranteed (see Appendix B for more details on the launch of the experiment). All were asked to respond to the phone surveys 12 and 24 months after enrolling. Finally, 20 0 0 young people were placed in the control group, and 60 0 0 were placed in the test group for the evaluation protocol. For the first survey, 828 individuals in the control group and 10 0 0 individuals in the test group were interviewed randomly. For the second survey, 629 individuals in the control group and 1270 in the test group were interviewed. Note that two

different random draws were held to select the young people to be interviewed for each survey. Consequently, the young people interviewed varied from one survey to the other. The overall protocol for the experiment is presented in Fig. 2.3 Local youth centers are dispersed throughout France and are located in various socio-economic contexts (from rural to urban areas). Fig. 3 presents the geographical distribution based on the young people’s postal codes. This broad geographical distribution, along with the variety of local economic and social contexts, is especially meaningful for a large and controlled experiment and reinforces its external validity. To ensure that our random assignment was successful in balancing the control and test groups, we compared the groups with respect to the observable pre-treatment characteristics in both surveys (Table 1). Globally, the randomization therefore produced a good balance between the groups. The young people in the experiment were 22 years old on average, had a low level of educational achievement, no work experience, little or no theoretical and practical knowledge of driving, still lived with their parents and were mostly unemployed. The test and control groups were similar in terms of gender, non-French citizenship, proportional compulsory education level, work experience, driving experience, moped ownership, ASR or BSR qualification,4 resources, occupational status and type of housing. The age difference was significant, however, while the mean age was very similar in both groups (22.9 vs. 22.76 years). The proportion appeared to be slightly higher in the test group for upper secondary education (0.169 vs. 0.138), but the difference was no longer significant when broken down by different educational categories (general, technological, vocational). Conversely, the proportion of university-educated young people was

3 A separate survey of the 154 local sites in contact with the young people involved was also conducted in 2012 to collect additional information about the local context, available financial assistance, and the type of non-monetary support in place. Other forms of available financial assistance varied considerably from one location to another. However, this assistance was not as substantial as the one offered by the experiment. We controlled for these differences in the evaluation by adding resource-based control variables. The overall results remain similar when including these additional controls. Complete results are available upon request. 4 The road safety certificate (Attestation de Sécurité Routière, ASR) is usually awarded in school and involves two levels validated after theoretical tests (ASSR1 and ASSR2). Level 1 provides access to practical training in a driving school, which in turn provides another certificate, required for driving a moped (Brevet de Sécurité Routière, BSR).

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J. Le Gallo et al. / Journal of Urban Economics 97 (2017) 1–14

Fig. 2. Evaluation protocol.

Fig. 3. Geographical coverage of the experiment. Note: the geocoding of the participants was performed based on the postal code of their residence.

J. Le Gallo et al. / Journal of Urban Economics 97 (2017) 1–14 Table 1 Balance of explanatory variables.

Women Age Foreign Educ – compulsory Education – upper sec Education – university Work experience No driving experience < 5 h driving experience > 5 h driving experience Moped ASR or BSR CIVIS Resources In job training Unemployed Employed Living with parents Independent housing Other housing

Test group

Control group

Difference

t test

0.561 22.935 0.093 0.484 0.169 0.016 0.790 0.648 0.149 0.202 0.120 0.201 0.646 304.084 0.123 0.725 0.152 0.655 0.236 0.109

0.573 22.759 0.103 0.499 0.138 0.030 0.807 0.667 0.147 0.185 0.105 0.207 0.673 286.231 0.123 0.748 0.128 0.633 0.248 0.119

−0.012 0.175 −0.009 −0.015 0.031 −0.013 −0.017 −0.019 0.002 0.017 0.015 −0.007 −0.027 17.854 −0.0 0 0 −0.023 0.024 0.022 −0.012 −0.009

−0.703 2.383∗∗ −0.951 −0.890 2.566∗∗ −2.564∗∗ −1.294 −1.203 0.143 1.319 1.383 −0.487 −1.692∗ 1.554 −0.0594 −1.588 2.081 1.359 −0.859 −0.888

Notes: Column 1 displays mean characteristics for the test group and column 2 for the control group. ∗∗∗ Significant at 1%. ∗∗ Significant at 5%. ∗ Significant at 10%.

slightly lower in the test group (0.016 vs. 0.030), but the frequency of that category was minimal (fewer than 20 individuals), so that each group had a similar level of educational achievement. Finally, we found a slightly higher number of individuals with a CIVIS contract5 in the test group (0.646 vs. 0.673), but the difference was only significant at the 10% level. Our aim is to identify the impact of the treatment “receiving a €10 0 0 voucher and the non-monetary aids by the welfare center” on three categories of outcomes contained in the surveys: 1 Driving outcome: success in the theoretical portion, success to the practical portion, and car ownership; 2 Employment outcomes: being employed, being permanently employed, being temporarily employed; 3 Housing outcomes: living in independent housing, moving within the last 12 months. We selected these three categories in order to measure the effects of the subsidy on the social integration and self-reliance of young people. This can be broken down into means of transportation and financial independence, which is linked to employment access, but also to independent housing. Indeed, the latter aspect is interesting to consider, as less favorable economic conditions (fewer jobs, lower wages and higher rental costs) lead to an increase in the numbers of young people living with their parents. In the US, the fraction of 24-years-olds living with their parents increased by 39% for men and 64% for women between 1970 and 20 0 0 (Matsudaira, 2016). In France, where young people are particularly affected by unemployment, the age at which youths form a household has increased since the 1980s: the proportion of 20 to 24-year-old young people living together as couples has dropped from 29% in 1982 to 16% in 2006 (CESE, 2013). During the evaluation, the pre-treatment characteristics were used to construct individual control variables for each outcome. Moreover, due to the substantial size of the controlled experiment, and a scope that covers the entire French territory, includ5 The CIVIS contract is an action plan aimed at helping young people with integration difficulties to join the workforce. When they subscribe to this contract, a case worker supports them in their career path. These contracts are signed in missions locales, or in information and careers guidance centres.

5

ing a fixed municipal effect would severely limit the degrees of freedom.6 Rather, we included fixed, region-specific effects (23) and combined the information drawn from the survey with other sources of administrative data to construct contextual variables specific to each category of outcome. These variables were measured at the young person’s lowest local government level (commune) and sought to measure transportation services (driving outcomes), tensions on the local housing market (housing outcomes), and tensions on the labor market (employment outcomes). Moreover, all outcomes included population density and its square in order to factor in the possible non-linear effects regarding this aspect. The definition and source of these contextual variables are presented in Table 2. 3. Results The impact of the €10 0 0 subsidy on several outcomes can be investigated using the following model:

Yi = β0 + β1 Ti + xi θ + εi

(1)

where Yi is the outcome of individual i, Ti is the indicator of being treated by receiving the €10 0 0 subsidy, and ε i is the error term. To ensure balance and residual variance, we also included the xi vector for control characteristics. This vector includes pre-treatment characteristics for each individual and certain specific contextual variables for each category of outcome, as described in Table 2 (see Section 2). In both surveys, Eq. (1) is estimated by Ordinary Least Squares (OLS) for each outcome, with and without control variables and with standard errors clustered at the local site level.7 Fixed regional effects were included in the models with controls. The results for each category of outcome (driving, housing, and employment), are presented in Sections 3.1, 3.2 and 3.3, respectively. In Section 3.4, we investigated the possibility of spillovers from treated to untreated individuals and discuss the general equilibrium aspects implied by our analysis. We have also investigated the potential of treatment heterogeneity by systematically interacting the treatment with the explanatory variables, in particular a gender dummy (using the value 1 for women), income, education and also an urban dummy (using the value 1 when the commune of residence is an urban unit, according to the definition contained in the French National Statistical Office) The interactions were never significant except for education in the driving outcomes. The results in this case are given in the next section while complete results with all possible interactions are available upon request. 3.1. Driving outcomes The estimation results for the three driving outcomes (passing the theoretical test, passing the practical test, and owning a car) are presented in Table 3. Four estimation results are presented for each outcome: two surveys, with and without control variables. For the theoretical test outcome, the sample was reduced as some individuals had already passed it before the experiment began. They were therefore removed from the sample. The €10 0 0 subsidy was clearly beneficial at each step of the learning process as the treatment coefficient is positive and significant for all three driving outcomes. For instance, the difference between treated and untreated individuals is about 0.2 when passing the theoretical test, a figure that remains stable in both surveys (respectively 53% and 66% for the test group, 34.2% and 47.2% 6

The total number of municipalities involved is 923. We have also performed the regressions with clustered robust standard errors at the municipal and regional levels. The results were not modified and are available upon request. 7

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J. Le Gallo et al. / Journal of Urban Economics 97 (2017) 1–14

Table 2 Contextual variables; communal level.

Population density Road density Railway density % Vacant housing New households % Unemployment Active/employed Active/firms

Definition

Source

Ratio of population over communal area in 2011 Ratio of kilometres of road over departmental area in 2011 Ratio of kilometres of railway over departmental area in 2011 Communal rate of vacant housing in 2010 Proportion of households having moved in the communes in 2 years before 2010 Unemployment rate in 2010 Ratio of active population to total number of jobs in commune in 2010 Ratio of active population to total number of firms in commune in 2010

General census (2011) General census (2011) General census (2011) INSEE (2010) INSEE (2010) INSEE (2010) INSEE (2010) INSEE (2010)

Table 3 OLS estimation results for driving outcomes. Theory test Survey 1

Practical test Survey 2

Survey 1

Car ownership Survey 2

Survey 1

Survey 2

0.2104∗∗∗ 0.2054∗∗∗ 0.2139∗∗∗ 0.2071∗∗∗ 0.1136∗∗∗ 0.1062∗∗∗ 0.1473∗∗∗ 0.1373∗∗∗ 0.0620∗∗∗ 0.0571∗∗∗ 0.1406∗∗∗ 0.1306∗∗∗ (0.0283) (0.0288) (0.0244) (0.0253) (0.0183) (0.0194) (0.0217) (0.0204) (0.0159) (0.0173) (0.0216) (0.0215) Women −0.0386 −0.0285 −0.0046 −0.0336 0.0163 −0.0133 (0.0264) (0.0272) (0.0161) (0.0236) (0.0142) (0.0243) ∗∗∗ ∗∗∗ ∗∗∗ ∗∗∗ −0.0135 −0.0202 −0.0145 −0.0210∗∗∗ Age −0.0034 −0.0196 (0.0063) (0.0061) (0.0047) (0.0055) (0.0039) (0.0050) −0.0071 −0.0295∗ −0.0522 −0.0251 −0.0518 Foreign −0.0722∗∗ (0.0348) (0.0393) (0.0273) (0.0304) (0.0218) (0.0378) 0.0048 0.0439∗ −0.0048 0.0447∗∗ Education – compulsory 0.0276 0.0483∗ (0.0255) (0.0272) (0.0178) (0.0273) (0.0156) (0.0225) 0.1931∗∗∗ 0.1037∗∗∗ 0.1153∗∗∗ 0.0617∗∗∗ 0.1357∗∗∗ Education – upper sec 0.1452∗∗∗ (0.0354) (0.0374) (0.0268) (0.0341) (0.0240) (0.0358) 0.3315∗∗∗ 0.097 0.2067∗∗∗ 0.0657 0.1342∗ Education – university 0.2730∗∗∗ (0.0851) (0.0734) (0.0758) (0.0668) (0.0682) (0.0796) 0.0080 0.0649∗∗∗ 0.0415 0.0634∗∗∗ 0.0711∗∗∗ Work experience 0.0772∗∗∗ (0.0315) (0.0334) (0.0256) (0.0275) (0.0209) (0.0253) < 5 h driving experience 0.0300 0.0145 0.0368 0.0211 0.0124 0.0064 (0.0324) (0.0269) (0.0225) (0.0221) (0.0255) (0.0221) ∗∗∗ ∗∗∗ ∗∗∗ ∗∗∗ ∗∗∗ 0.0875 0.1443 0.1612 0.1041 0.1355∗∗∗ > 5 h driving experience 0.1369 (0.0247) (0.0278) (0.0215) (0.0205) (0.0208) (0.0201) 0.0790∗ 0.0885∗∗∗ 0.118∗∗∗ Moped 0.0103 0.0682 0.1313∗∗∗ (0.0415) (0.0445) (0.0313) (0.0418) (0.0264) (0.0381) ASR or BSR 0.0041 −0.0108 0.0010 0.0485 0.0260 0.0131 (0.0325) (0.0302) (0.0223) (0.0299) (0.0211) (0.0292) −0.0520∗∗ −0.0463∗∗ −0.0308 CIVIS −0.0123 −0.0021 −0.0625∗∗∗ (0.0244) (0.0233) (0.0201) (0.0253) (0.0193) (0.0244) Resources −4.74e−06 1.26e−06 −1.47e−05 −7.44e−06 −3.61e−05 8.74e−06 (4.16e−05) (4.07e−05) (3.18e−05) (3.45e−05) (2.52e−05) (3.35e−05) Employed −0.0148 −0.0050 −0.0288 0.0043 −0.0079 0.0137 (0.0401) (0.0388) (0.0322) (0.0327) (0.0292) (0.0312) In job training −0.0356 0.0071 −0.0169 0.0399 −0.0107 −0.0126 (0.0349) (0.0377) (0.0275) (0.0310) (0.0213) (0.0312) ∗ 0.0096 0.0377 −0.0494 0.0532 −0.0259 0.0399 Independent housing (0.0405) (0.0417) (0.0293) (0.0419) (0.0272) (0.0415) 0.0266 −0.0579∗∗ 0.0035 Parental housing −0.0320 −0.0103 −0.0584∗∗ (0.0358) (0.0376) (0.0270) (0.0332) (0.0239) (0.0362) −2.71e−05∗∗ −3.92e−05∗∗∗ −4.84e−07∗∗∗ −3.18e−05∗∗∗ −4.90e−05∗∗∗ Population density −3.22e−05∗∗∗ (1.15e−05) (1.08e−05) (9.9e−06) (1.06e−05) (7.92e−06) (1.01e−05) 2.67e−09∗∗∗ 1.95e−09∗∗∗ 2.77e−09∗∗∗ Pop density squared 1.65e−09 6.74e−10 2.67e−09∗∗∗ (1.02e−09) (7.92e−10) (9.21e−10) (9.62e−10) (5.67e−10) (9.15e−10) Road density 0.0639 0.0055 −0.0445 0.0067 −0.0406 0.0538 (0.0667) (0.0692) (0.0474) (0.0536) (0.0407) (0.0422) 0.6477 −1.321 Railway density −1.6900 −0.1073 0.6173 −0.4310 (1.3037) (1.3694) (0.929) (1.0775) (0.7960) (0.823) 0.3985∗∗∗ 0.8676∗∗∗ 0.1371∗∗∗ 0.6452∗∗∗ 0.2955∗∗∗ 0.9046∗∗∗ 0.0995∗∗∗ 0.5791∗∗∗ 0.2556∗∗∗ 0.7973∗∗∗ Constant 0.2422∗∗∗ 0.4618∗∗ (0.0174) (0.1903) (0.0187) (0.2157) (0.0186) (0.1638) (0.0293) (0.1901) (0.0159) (0.1198) (0.0249) (0.1524) Treatment

Region fixed effects

No

Number of observations 1561 Adjusted R2 0.048

Yes

No

Yes

No

Yes

No

Yes

No

Yes

No

Yes

1561 0.106

1626 0.041

1626 0.084

1821 0.020

1821 0.153

1893 0.020

1893 0.145

1821 0.008

1821 0.106

1893 0.019

1893 0.138

Notes: OLS; standard errors clustered at the local site level. ∗∗∗ Significant at 1%. ∗∗ Significant at 5%. ∗ Significant at 10%.

J. Le Gallo et al. / Journal of Urban Economics 97 (2017) 1–14

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Table 4 Conditional probabilities. 12 month effect (survey 1)

Passed theory test ... first time Passed practical test ... first time Total number of driving hours

24 months effect (survey 2)

Test

Control

Difference

Std. dev.

p-value

Test

Control

Difference

Std. dev.

p-value

53.00% 65.09% 47.64% 62.70% 24.36

34.18% 62.19% 40.07% 58.41% 24.63

18.82% 2.90% 7.57% 4.29% −0.27

8.20 0.82 2.07 0.78 0.17

0.0 0 0 0 0.4117 0.0392 0.4377 0.8687

66.06% 62.05% 67.90% 57.04% 32.21

47.22% 62.80% 63.39% 53.51% 24.63

18.84% −0.75% 4.51% 3.53% 7.58

8.01 0.23 1.41 0.84 3.71

0.0 0 0 0 0.8200 0.1577 0.4024 0.0 0 03

for the control group). However, the effect is higher in the second survey, both for practical test (around 0.11 in the first survey, and 0.14 in the second), and moreover for owning a car (0.06 in the first survey, and 0.14 in the second). These figures can be applied to the overall experiment and provides an order of magnitude for the effects. Two years after the subsidy was granted to 10,0 0 0 individuals, roughly 2100 of them did not pass the theoretical test without help, approximately 1400 did not pass the practical test, and 1300 did not own a car. While subsidies and non-monetary support have important positive effects on passing the theoretical test, practical test and car ownership, the chances remain low in absolute terms, and more so when considering that every young person volunteered to participate in the experiment. Two years after it began, one young person in two failed the theoretical test, one in two failed the practical test and one in three did not own a car. These figures illustrate the major difficulties facing young people with integration problems when seeking access to vehicle use in France. Turning to the individuals’ pre-treatment characteristics, other things being equal, it was easier for younger and more educated individuals to pass the theoretical test, the practical test and to own a car. Having more than five hours of previous driving experience also had a positive impact on the outcome, while previous work experience had a strong positive effect. Some discrimination against non-French citizens was also apparent in the theoretical and practical tests, which might reflect an inability to master the French language when taking the tests. With respect to environmental characteristics, population density had a noticeable nonlinear effect on outcomes, with an initial negative impact up to an approximate threshold of 80 inhabitants per km², followed by a positive impact. In order to understand these results, we calculated the conditional probabilities of success, i.e. the probability of moving on to the next stage of vehicle use for those who passed the previous stage. The results are presented in Table 4. The proportion of young people who passed the theoretical test on their first, second or third attempt is identical in both groups and in both surveys. Thus, subsidies and support do not increase the chances of passing the theoretical test. Young people in the test group had a higher success rate in the theoretical test because they were able to take the test more than once. Similarly, for those who passed the theoretical test, the treatment noticeably improved their chances in the practical test. Indeed, the pass rate for the practical test was 47.6% for treated young people, versus 40.1% for the rest, with a significant difference in the first survey (but not in the second). However, the proportion of young people that passed the practical test on their first attempt is similar in both groups and in both surveys. Thus, subsidies and support do not increase the passing rate for the practical test, but do allow the candidates to take the test more often. This is confirmed by the fact that the treated young people took part in more driving lessons: 32.2 h 24 months after the beginning of the experiment, as compared to 24.6 h for those in the control group. In addition to providing information on whether or not the treatment and control groups were comparable on observables,

Table 5 presents the types of people who were induced to obtain a driver’s license through to this intervention. The differences were few but nevertheless interesting. Firstly, the test group youths who successfully passed the theoretical and practical tests were younger than those in the control group, which is related to the fact that the treatment allowed youths from the test group to obtain the license earlier than the others. Secondly, there is no difference in the percentage between the test and control groups for youths with a compulsory level of education, while a greater number of youths with upper secondary level education in the control group successfully passed the theoretical test. The same was true for test group youths with a university level education. The exact opposite was true for the practical test. This means that the treatment is more influential when helping more highly educated young people successfully pass the theoretical test (there were very few in our sample). The treatment was equally influential for upper secondary level youths when helping them successfully complete the practical test. One also notices how the treatment was better able to help youths with fewer resources, along with those who obtained support from the missions locales through a CIVIS contract. Since these results point to differences due to education levels, we investigated the potential of treatment heterogeneity with respect to education by interacting the treatment with the 3 education dummies corresponding to the compulsory, upper secondary and university levels. The results are displayed in Table 6 where only the coefficients for the treatment, the education dummies and the interaction variables are shown as the significance and size of the other coefficients were not modified. Results indicate that the difference between treated and untreated individuals drops to 0.16 when passing the theoretical test and to 0.07 for passing the practical tests for the reference youths, i.e. youth with no education. Conversely, treated youths with upper secondary level have a significant higher probability of succeeding to the theoretical (in the second year) and practical (for both years) tests. Indeed, for this category of education level, the difference between treated and untreated individuals is around 0.38 for the theoretical test for the second survey and around 0.2 (first survey) and 0.25 (second survey) for the practical test. 3.2. Employment outcomes The estimation results for the three employment outcomes (being employed, being permanently employed, and being temporarily employed) are presented in Table 7. Globally, the effects of the subsidy on employment were very limited.8 Primarily, treated individuals were less likely to be employed or permanently employed one or two years after the program. The subsidy only appears to

8 We calculated the Minimum Detectable Effect (MDE) for each case. For the employment outcomes, the MDE was roughly equal to 0.117 in the model without covariates and 0.115 in the model with covariates when the power is set to 80% and the significance level to 5%. For a power of 50%, the MDE was approximately 0.076. Thus, the absence of significance for the treatment may also be due to the low power of the test for these outcomes. At any rate, these results suggest that the effect of the treatment is, at best, very limited.

8

J. Le Gallo et al. / Journal of Urban Economics 97 (2017) 1–14 Table 5 Characteristics of people having succeeded to the theory and practical tests. Theory test

Women Age Foreign Educ – compulsory Education – upper sec Education – university Work experience No driving experience < 5 h driving experience > 5 h driving experience Moped ASR or BSR CIVIS Resources In job training Unemployed Employed Living with parents Independent housing Other housing

Practical test

Test group

Control group

Difference

t-test

Test group

Control group

Difference

t-test

0.548 22.491 0.083 0.496 0.128 0.047 0.794 0.653 0.149 0.175 0.141 0.248 0.718 272.138 0.099 0.760 0.141 0.655 0.219 0.110

0.528 23.042 0.086 0.494 0.185 0.022 0.811 0.702 0.149 0.148 0.144 0.225 0.658 305.256 0.112 0.734 0.154 0.633 0.256 0.111

0.020 −0.552 −0.002 0.002 −0.057 0.024 −0.017 −0.049 −0.0 0 0 0.026 −0.003 0.023 0.059 −33.118 −0.012 0.026 −0.013 0.022 −0.037 −0.001

0.686 4.304∗∗∗ −0.153 0.075 −2.756∗∗ 2.066∗∗ −0.712 −1.750∗ −0.014 1.183 −1.345 0.895 2.185∗∗ −1.657∗ −0.686 0.996 0.630 1.349 −1.478 −0.055

0.550 22.947 0.052 0.487 0.218 0.022 0.819 0.528 0.149 0.321 0.174 0.249 0.604 301.879 0.148 0.711 0.140 0.665 0.242 0.094

0.523 22.486 0.070 0.500 0.137 0.044 0.799 0.490 0.168 0.342 0.188 0.268 0.601 263.879 0.151 0.718 0.131 0.671 0.211 0.117

0.026 0.460 −0.019 −0.013 0.081 −0.021 0.020 0.038 −0.020 −0.022 −0.014 −0.019 0.003 37.123 −0.003 0.006 0.010 −0.006 −0.030 −0.024

0.781 3.243∗∗∗ −1.114 −0.382 3.266∗∗ −1.657∗ 0.746 1.115 −0.806 −0.677 −0.535 −0.649 0.106 1.625 −0.125 0.217 0.420 −0.205 1.078 −1.114

Notes: Columns 1 and 5 display mean characteristics for the treated people having succeeded to the theory and the practical tests respectively. Columns 2 and display mean characteristics for the non-treated people having succeeded to the theory and the practical tests respectively. ∗∗∗ Significant at 1%. ∗∗ Significant at 5%. ∗ Significant at 10%.

Table 6 OLS estimation results for driving outcomes with heterogeneity on treatment with education. Theory test

Practical test

Survey 1 Survey 2 Treatment

∗∗∗

∗∗∗

0.167 0.151 (0.040) (0.044) Education – compulsory 0.001 0.009 (0.039) (0.046) Education – upper sec 0.085 0.030 (0.056) (0.071) 0.414∗∗∗ Education – university 0.265∗∗ (0.111) (0.135) 0.060 Education – compulsory∗ treatment 0.048 (0.052) (0.057) ∗ 0.107 0.230∗∗∗ Education – upper sec treatment (0.074) (0.084) 0.009 −0.145 Education – university∗ treatment (0.170) (0.175) 0.935∗∗∗ Constant 0.498∗∗∗ (0.171) (0.182) Controls Yes Yes Number of observations 1561 1626 0.130 0.112 R2

Survey 1 ∗∗

0.063 (0.030) −0.021 (0.029) 0.026 (0.041) 0.113 (0.081) 0.046 (0.039) 0.137∗∗ (0.054) −0.059 (0.129) 0.687∗∗∗ (0.130) Yes 1821 0.175

and/or permanently employed. Again, a congestion effect becomes apparent through the negative sign of population density. 3.3. Housing outcomes

Survey 2 0.077∗∗ (0.039) −0.001 (0.041) −0.006 (0.060) 0.170 (0.108) 0.068 (0.050) 0.174∗∗ (0.071) 0.057 (0.144) 0.961∗∗∗ (0.162) Yes 1821 0.166

Notes: OLS with standard errors clustered at the local site level. ∗∗∗ Significant at 1%. ∗∗ Significant at 5%. ∗ Significant at 10%.

The estimation results for the two housing outcomes (living in independent housing, having moved in the last 12 months) are presented in Table 8. While the effect of subsidies is significantly positive one year after they were given, showing a difference of approximately 0.13 between treated and untreated individuals with respect to independent housing, it became slightly negative (−0.05) after two years. With respect to moving, the effect was significant and negative for both years, although higher in absolute value for the first year (roughly −0.07 and −0.03, respectively). This may highlight the program’s lock-in effect: young people must stay at the same local site throughout the learning period in order to obtain subsidies and benefits from non-monetary support. This limits their residential mobility.9 The effects of control variables are quite similar in both outcomes. Other things being equal, women were more likely to be in independent housing for both years and, not surprisingly, individuals who were not living with their parents during the program were more likely to live in independent housing, or to move, 1 and 2 years after the program. Finally, population density was significantly negative, highlighting a congestion effect in the housing market within high-density areas. 3.4. Spillovers and general equilibrium effects

have had a slightly positive and significant impact two years after for access to temporary employment, with a difference of 0.03. With respect to the control variables, other things being equal, the level of education is positive and strongly significant for the first and third outcomes, reflecting the importance of this factor when finding work, with a greater impact on the few young people with a university education, as expected. High inertia also appears, as individuals who were already employed during the program were more likely to be temporarily or permanently employed. Individuals with employment experience were more likely to be employed

We evaluated an experimental device aimed at reducing the cost of the driver’s license for young NEET people. The experiment was consistently deployed locally and punctually. We know 9 We have checked that this negative effect on the housing autonomy is not related to the previous effect on temporary jobs. Among people who are living in an independent housing, the share of those occupying a temporary job varies very little between the two surveys (it rose from 15.3% to 16.9%). The two variables, living in an independent housing and occupying a temporary employment, are independent in the meaning of a chi squared test.

J. Le Gallo et al. / Journal of Urban Economics 97 (2017) 1–14

9

Table 7 Estimation results for employment outcomes. Employed

Permanent job

Survey 1 Treatment

−0.0148 (0.0221)

Women Age Foreign Education – compulsory Education – upper sec Education – university Work experience < 5 h driving experience > 5 h driving experience Moped ASR or BSR CIVIS Resources Employed In job training Independent housing Parental housing Population density Pop density squared % Unemployment Active/employed Active/establishment Constant Region fixed effects

0.3106∗∗∗ (0.0150) No

Number of observations 1821 R2 0.0 0 0

Survey 2

Survey 1

−0.0193 −0.0047 (0.0135) (0.0150) 0.0037 (0.0127) 0.00198 (0.0034) −0.0133 (0.0284) 0.0240 (0.0161) 0.0105 (0.0175) 0.0669∗∗ (0.0313) 0.0346∗∗∗ (0.0126) 0.0060 (0.0164) 0.0112 (0.0126) 0.0198 (0.0228) −0.0135 (0.0174) 0.0046 (0.0134) −2.75e−05 (2.14e−05) 0.1051∗∗∗ (0.0254) −0.0016 (0.0199) 0.0287 (0.0264) −0.0324 (0.0207) 1.04e−05 (7.09e−06) −1.04e−10∗∗ (5.21e−10) 1.54e−06 (1.46e−05) 8.29e−06 (1.16e−05) 6.31e−06 (1.18e−05) 0.0586 0.1278∗∗∗ (0.0818) (0.0127)

Survey 1 −0.0060 −0.0192 (0.0153) (0.0189) 0.0087 (0.0153) −0.0 0 06 (0.0039) −0.0081 (0.0256) 0.0246 (0.0165) 0.0299 (0.0255) −0.0514 (0.0528) 0.0314∗ (0.0179) 0.0043 (0.0187) −0.0 0 07 (0.0140) 0.0476 (0.0288) −0.0443∗∗ (0.0193) −0.0333∗ (0.0179) 9.45e−06 (2.81e−05) 0.00731 (0.0259) −0.0063 (0.0251) −0.0104 (0.0319) −0.0536∗∗ (0.0268) 8.81e−06 (6.22e−06) −6.80e−10∗∗ (3.40e−10) −4.56e−06 (1.41e−05) −6.97e−06 (1.42e−05) −6.38e−06 (1.11e−05) 0.2154 0.1626∗∗∗ (0.1106) (0.0130)

Survey 2 −0.0208 (0.0202) 0.0245 (0.0199) 0.0112∗∗∗ (0.0043) −0.0062 (0.0272) 0.0302 (0.0189) 0.0406 (0.0265) 0.0907 (0.0689) −0.0047 (0.0223) −0.0306 (0.0187) 0.0070 (0.0155) 0.0265 (0.0308) 0.0198 (0.0224) 0.0127 (0.0202) 1.60e−05 (3.33e−05) 0.08434∗∗∗ (0.0306) 0.0029 (0.024) −0.0328 (0.0317) 0.0019 (0.0290) 1.17e−05 (9.14e−06) −1.07e−09 (6.66e−10) 1.04e−06 (1.83e−05) 4.32e−06 (1.57e−05) −1.78e−05 (1.45e−05) −0.1635 (0.1084)

0.0308∗ (0.0170)

0.0322∗ (0.0171) 0.0114 (0.0206) 0.0015 (0.0041) 0.0369 (0.0291) 0.0493∗∗∗ (0.0170) 0.0732∗∗∗ (0.0271) 0.217∗∗∗ (0.0762) 0.0387∗ (0.0222) −0.0132 (0.0145) −0.0207 (0.0205) 0.0051 (0.0250) −0.0259 (0.0201) 0.0208 (0.0180) −3.07e−06 (3.32e−05) 0.0480 (0.0315) 0.0198 (0.0245) 0.0190 (0.0302) 0.0209 (0.0279) −2.28e−06 (6.51e−06) 1.07e−11 (3.75e−10) −4.00e−05∗ (1.92e−05) 1.47e−05 (1.40e−05) −1.31e−05 (1.66e−05) 0.0264 (0.1106)

−0.0193 (0.0223) −0.0054 (0.0248) 0.0116∗ (0.0064) −0.0076 (0.0409) 0.0571∗∗ (0.0241) 0.0745∗∗ (0.0329) 0.0448 (0.0875) 0.0329 (0.0255) −0.0390 (0.0271) 0.0179 (0.0198) 0.0405 (0.0348) 0.0187 (0.0288) 0.0078 (0.0238) −1.92e−05 (4.39e−05) 0.01896 (0.0393) −0.0052 (0.0348) −0.0231 (0.0370) −0.0532 (0.0365) 1.58e−05∗∗ (1.08e−06) −1.90e−09∗∗ (7.67e−10) −9.02e−07 (2.67e−05) −5.14e−07 (1.93e−05) −1.17e−06 (1.96e−05) 0.0515 (0.165)

0.3258∗∗∗ (0.0191)

Yes

No

Yes

No

Yes

No

Yes

No

Yes

No

Yes

1821 0.029

1893 0.0 0 0

1893 0.044

1821 0.001

1821 0.034

1893 0.0 0 0

1893 0.016

1821 0.001

1821 0.024

1893 0.002

1893 0.026

0.0167 (0.0255)

0.0172 −0.0146 (0.0252) (0.0140) −0.0340 (0.0232) −0.0 0 07 (0.0048) 0.04205 (0.0352) 0.0805∗∗∗ (0.0249) 0.1269∗∗∗ (0.0356) 0.1939∗∗ (0.0833) 0.1067∗∗∗ (0.0270) −0.00595 (0.0241) −0.0103 (0.0194) 0.0654∗ (0.0382) −0.0652∗∗ (0.0261) −0.00714 (0.0242) 2.76e−05 (4.33e−05) 0.1188∗∗∗ (0.0366) −0.0212 (0.0353) −0.0 0 03 (0.0412) −0.0452 (0.0369) 5.02e−07 (7.10e−06) −2.19e−10 (5.31e−10) −3.06e−05 (2.31e−05) −6.86e−06 (2.09e−05) −2.67e−05 (1.99e−05) 0.3586∗∗∗ 0.0959∗∗∗ (0.1372) (0.0109)

Temporary job Survey 2

0.1294∗∗∗ (0.0130)

Notes: OLS; standard errors clustered at the local site level ∗∗∗ Significant at 1%. ∗∗ Significant at 5%. ∗ Significant at 10%.

that the generalization of an experiment can cause multiple equilibrium effects through market and prices adjustments. This must be taken into consideration before recommending any such extension. If driver’s licenses become cheaper for all young people, and if youth mobility increases everywhere, this would probably impact household and firm location decisions, wages, prices and rent. The effects of all these adjustments will probably modify the shortterm impact of driver’s licenses on employment for young people. While all of these general equilibrium mechanisms are beyond the scope of this paper, we were able to consider some of the relevant ones in the short-term through an analysis of spillover effects. Specifically, the results of the previous sections were based on the standard Stable Unit Treatment Value Assumption (SUTVA).

Thus, this section seeks to measure the possibility of spillovers between treated and untreated individuals. Indeed, as both treated and untreated young people were monitored by the same local site, they were able to communicate and exchange information. We used the method set out by Baird et al., (2014) to control for possible spillover effects among treated and untreated young people.10 These authors argue that a randomized saturation design, which

10 Other authors identified network effects using experimental variation across treatment groups (Miguel and Kremer, 2004; Bobba and Gignoux, 2013). Some exploit plausibly exogenous variations within network treatments (Babcock and Hartman, 2010), or control for spatial spillovers by creating a radius around each treated individual (Bobba and Gignoux, 2013).

10

J. Le Gallo et al. / Journal of Urban Economics 97 (2017) 1–14 Table 8 OLS estimation results for housing outcome. Independent housing Survey 1 Treatment

0.1269∗∗∗ (0.0217)

Women Age Foreign Education – compulsory Education – upper sec Education – university Work experience < 5 h driving experience > 5 h driving experience Moped ASR or BSR CIVIS Resources Employed In job training Independent housing Parental housing Population density Pop density squared % Vacant housing New households

Moved in last 12 months Survey 2

0.14∗∗∗ (0.0169) 0.0491∗∗ (0.0233) 0.0161∗∗∗ (0.0054) 0.0914∗∗ (0.0393) 0.0458∗ (0.0977) 0.0294 (0.0379) 0.0899 (0.0735) 0.0055 (0.0296) 0.0112 (0.0261) 0.00623 (0.0180) 0.0388 (0.0329) −0.0168 (0.0268) −0.0175 (0.0254) 2.53e−05 (4.0e−05) 0.0041 (0.0313) −0.0013 (0.032) 0.348∗∗∗ (0.0416) −0.140∗∗∗ (0.0397) −2.71e−05∗∗∗ (9.84e−05) 1.39e−09∗ (9.38e−10) 1.60e−05 (1.58e−05) −7.82e−06 (2.01e−05) 0.0235 (0.1378)

−0.0509∗∗∗ (0.0188)

0.3003∗∗∗ (0.0176)

Survey 1 −0.0547∗∗∗ (0.0183) 0.0716∗∗∗ (0.0207) 0.0 0 06 (0.0054) −0.00766 (0.0346) −0.00713 (0.0240) 0.0248 (0.031) −0.1340∗∗ (0.0616) 0.0466∗∗ (0.0216) 0.0018 (0.0241) 0.0350∗∗ (0.0192) −0.0583∗ (0.0324) −0.0060 (0.0253) −0.00335 (0.0214) 4.49e−05 (4.13e−05) −0.0046 (0.0349) 0.00218 (0.0310) −0.161∗∗∗ (0.0398) −0.303∗∗∗ (0.0345) −6.34e−06 (7.30e−06) 2.94e−10 (5.93e−10) 2.50e−06 (1.79e−05) 1.47e−05 (1.73e−05) 0.3769∗∗∗ (0.1454)

−0.0804∗∗∗ (0.0186)

0.2379∗∗∗ (0.0155)

Survey 2 −0.0655∗∗∗ (0.0174) 0.0031 (0.0190) −0.0116∗∗ (0.0049) −0.0 0 05 (0.0378) 0.0605∗∗∗ (0.0206) 0.0406 (0.0312) 0.0960 (0.0690) 0.0555∗∗∗ (0.0202) 0.0066 (0.0233) 0.0279 (0.0165) −0.0109 (0.0308) −0.0096 (0.0274) −0.0115 (0.0219) −2.41e−05 (3.27e−05) 0.0130 (0.0279) −0.0223 (0.0286) −0.064 (0.0454) −0.241∗∗∗ (0.0373) −2.32e−06 (9.38e−06) 4.65e−10 (7.46e−10) −1.90e−05 (1.90e−05) −1.85e−05 (1.85e−05) 0.6091∗∗∗ (0.1358)

−0.0363∗ (0.0204)

0.3307∗∗∗ (0.0189)

−0.0390∗ (0.0220) 0.0554∗∗∗ (0.0208) −0.0048 (0.0059) −0.0107 (0.0350) −0.01179 (0.0242) 0.02485 (0.0326) −0.0975 (0.0621) 0.0329 (0.0239) −0.0078 (0.0250) 0.01335 (0.0201) −0.0661 (0.0343) 0.02002 (0.0274) −0.0094 (0.0233) −2.45e−05 (4.09e−05) 0.0123 (0.0333) 0.0483 (0.0329) −0.1492∗∗∗ (0.0394) 0.3130∗∗∗ (0.0352) −5.28e−06 (7.27e−06) 1.27e−10 (5.45e−10) 1.27e−05 (1.99e−05) 1.05e−06 (1.87e−05) 0.5688∗∗ (0.1590)

Constant

0.4247∗∗∗ (0.0189)

Region fixed effects

No

Yes

No

Yes

No

Yes

No

Yes

Number of observations R2

1821 0.016

1821 0.234

1893 0.003

1893 0.081

1821 0.010

1821 0.077

1893 0.001

1893 0.067

Notes: OLS; standard errors clustered at the local site level. ∗∗∗ Significant at 1%. ∗∗ Significant at 5%. ∗ Significant at 10%.

involves an experimental variation of the rate of treated individuals between clusters, reveals spillovers. In our case, the clusters were the local sites. They also provide a method that can estimate the counterfactual situation when no pure control outcome is available. We applied this here, since the program design does not incorporate pure control clusters, i.e. clusters in which the saturation rate is zero. For that purpose, we calculated the saturation rate for each local site by dividing the total number of young people who actually benefited from the total number of locally eligible young people. The latter was calculated from the number of young people in each locality from census data, multiplied by the national proportion of licensed drivers among all young people, and again by the proportion of young people with integration problems among all young

people. The density of their distribution over the local site is presented in Fig. 4. There is a primary mode near 10% saturation, and a secondary mode near 45% saturation. The distribution is highly skewed to the right. Nearly two-thirds of the sites include fewer than 50 young people and are thus characterized by an often weak saturation rate. Among the experiment sites that included many young people, some were located in rural areas or small towns, leading to high levels of saturation (e.g. Bondy, Seine-Saint-Denis, with 131 young people and a saturation rate of 67%, La Seyne, Var, with 135 young people and a saturation rate of 64%, and Perpignan, with 233 young people and an estimated 74% saturation rate). Other sites that attracted an equal number of young people were located in densely populated areas, leading to low saturation rates (as in Venissieux, south of Lyon, where the saturation level was

J. Le Gallo et al. / Journal of Urban Economics 97 (2017) 1–14

Fig. 4. Density of saturation rates over the 154 local sites. Note: the density plot with the density function is estimated with a Gaussian kernel. Table 9 Spillovers on the non-treated; driving outcomes. Theory test Survey 1 ∗∗∗

Treatment Saturation Saturation

∗

Treatment

Constant

0.246 (0.0451) 0.0272 (0.0990) −0.187 (0.161) 0.221 (0.172)

Practical test Survey 2 ∗∗∗

0.224 (0.0404) −0.123 (0.0961) −0.0897 (0.150) 0.795∗∗∗ (0.155)

Survey 1 ∗∗∗

0.128 (0.0312) 0.122 (0.125) −0.0857 (0.0999) 0.429∗∗∗ (0.119)

Survey 2 0.192∗∗∗ (0.0343) 0.179 (0.170) −0.225∗∗ (0.104) 0.826∗∗∗ (0.151)

Controls

Yes

Yes

Yes

Yes

Number of observations R2

1561 0.117

1626 0.095

1821 0.151

1893 0.148

Notes: OLS with standard errors clustered at the local site level. ∗∗∗ Significant at 1%. ∗∗ Significant at 5%. ∗ Significant at 10%.

only 9% for 154 young people, or in Saint-Etienne, at 8% with 139 young people). Overall, it seems reasonable to assume that the saturation distribution is random. Formally, in the absence of a pure control cluster, Baird et al., (2014) suggest using estimates from the following equation:

Yim = α0 + α1 Tim + α2 πm + α2 (Tim ∗ πm ) + xim θ + εim

(2)

where the additional subscript m indicates the mth local site, and π m is the saturation rate of the mth local site. In the random saturation design with no pure control, the hypothesis test α 2 = 0 indicates whether or not there is a variation in the control outcome across saturations. If this hypothesis is rejected, then spillovers will appear in the untreated individuals and require corrections for the counterfactual. In this case, the unbiased estimate of the average total effect is equal to βˆ1 + βˆ0 − αˆ 0 , where βˆ0 and βˆ1 are the estimated coefficients in Eq. (1) estimated by weighted least squares, using the saturation rates and weights. The spillovers on the untreated individuals can be estimated as βˆ0 − αˆ 0 . Tables 9–11 show the OLS estimation results of Eq. (2) for all the outcomes with controls and standard errors clustered at the local site level and fixed regional effects. To save space, the estimation results for the control variables are not shown. For the driving

11

outcomes, the coefficient α 2 is never significant, so spillovers on the treated subjects are not detected. In the second survey, however, the interaction coefficient between saturation rate and treatment is significant and negative, which may highlight a congestion effect and delays for young people seeking a driving test. Indeed, examiner availability is required for the practical test. However, the number of local examiners is limited, which may explain a negative spillover on untreated young people. For the employment outcomes, the coefficient α 2 is never significant. Like the driving test, however, we notice that Survey 2 presents a significant 10% interaction effect between saturation and treatment, and a negative one for the first two outcomes (being employed and being permanently employed) in the second survey. Again, this may highlight some congestion effect on the local job market. We cannot exclude that positive employment outcomes are partly due to the fact that treated young people are taking jobs opportunities away from young people in the control group. Finally, for the housing outcomes, the coefficient α 2 is only significant at the 10% level in the first survey for the first outcome (living independently). In this case, we re-estimated Eq. (1) with weighted least squares11 to calculate the unbiased effect. It was −0.1167, corresponding to a negative spillover on the treated effect of 0.2467. The lock-in effect detected in the second survey therefore seems to be already present in the first survey. These negative spillover effects for both driving and employment outcomes urge caution when recommending the generalization of the program for all young people. Through equilibrium channels, the effects for each young person in a nation-wide program, such as lower permit costs for all young NEETs, for example, will be lower than those that were detected in the experiment. 4. Conclusion Social welfare arguments are often put forward to support targeted accessibility interventions. One of the most widely recommended actions has been to reduce the cost of drivers’ education and obtaining licenses for the most vulnerable socio-economic groups. This recommendation has been made in many countries, including the United States (Cervero et al., 2002.), the UK (Church et al., 20 0 0; Lucas, 20 06; Preston and Raje, 2007), France (Bertrand, 2005; Fol et al., 2007; Avrillier et al., 2010) and Spain (Cebollada, 2009), among others. Moreover, by assessing the link between expensive drivers’ education and its substitution elasticity with the alternative of relying on public transportation, Priya and Uteng (2009) show that when the cost of driving lessons is prohibitively high for certain groups, improved public transportation networks may, surprisingly, worsen social exclusion. Does lowering the cost of driving lessons improve access to employment? What are the effects of cutting these costs on the least privileged socio-economic groups? Should the process of obtaining the driver’s license be subsidized? In this paper, we carry out a large and randomized controlled experiment to assess the impact of improving daily mobility, as opposed to the impact of improving employment, education or training, on several outcomes, including driving, housing and employment status. Two years after participating in the program, one in three young people failed the theoretical test, more than one in two failed the practical test, and nearly two in three did not own cars. With a budget of €10 million for 10,0 0 0 young people, 1400 driver’s licenses were issued that would have otherwise not been obtained without assistance. This represents a cost of nearly €7150 per license, which is more or less five times the typical cost of driving lessons. The high cost argues against generalizing this type

11

The estimation results are available upon request.

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J. Le Gallo et al. / Journal of Urban Economics 97 (2017) 1–14 Table 10 Estimation results for employment outcomes; Spillovers on the non-treated. Employed

Treatment Saturation Saturation

∗

Treatment

Constant

Permanent job

Temporary job

Survey 1

Survey 2

Survey 1

Survey 2

Survey 1

Survey 2

0.0215 (0.0367) 0.0669 (0.0742) −0.152 (0.112) −0.100 (0.158)

0.0594 (0.0376) 0.0737 (0.0826) −0.190∗ (0.150) 0.225∗ (0.122)

−0.00610 (0.0226) 0.0328 (0.0440) −0.0335 (0.0710) −0.0840 (0.0857)

0.0188 (0.0239) 0.0903 (0.0573) −0.107∗ (0.0626) 0.0493 (0.0908)

−0.0104 (0.0328) 0.0175 (0.0611) −0.0384 (0.0950) −0.144 (0.101)

0.0350 (0.0287) −0.0428 (0.0765) −0.0152 (0.0965) 0.0470 (0.104)

1821 0.024

1893 0.027

Controls

Yes

Yes

Yes

Yes

Number of observations R2

1821 0.043

1893 0.045

1821 1821

1893 0.030

Notes: OLS with standard errors clustered at the local site level. ∗∗∗ Significant at 1%. ∗∗ Significant at 5%. ∗ Significant at 10%.

Table 11 Estimation results for housing outcomes; Spillovers on the non-treated. Independent housing Survey 1 ∗∗∗

Treatment Saturation Saturation

∗

treatment

Constant

0.106 (0.0306) −0.166∗ (0.0842) 0.141 (0.0983) −0.0233 (0.133)

Moved in last 12 months

Survey 2 ∗∗

−0.0706 (0.0311) −0.0899 (0.0765) 0.0603 (0.0864) 0.143 (0.135)

Survey 1 ∗∗∗

−0.0885 (0.0320) −0.0479 (0.0867) 0.0761 (0.0846) 0.369∗∗∗ (0.123)

Survey 2 −0.0811∗∗ (0.0333) −0.131 (0.0865) 0.177∗ (0.0939) 0.357∗∗ (0.154)

Controls

Yes

Yes

Yes

Yes

Number of observations R2

1821 0.241

1893 0.090

1821 0.077

1893 0.075

Notes: OLS with standard errors clustered at the local site level. ∗∗∗ Significant at 1%. ∗∗ Significant at 5%. ∗ Significant at 10%.

of intervention on a grander scale. More generally, it suggests that the funding systems for driving lessons that are operated by the central government and local governments, which are less intensive and less generous than the "Dix mille permis pour réussir" program, probably lead to even more modest effects. However, we should not conclude that this experiment has been a failure. If the mechanism had been generalized without having been subjected to prior evaluation, the public cost would have been substantial. To fund driving lessons for 150,0 0 0 young French people without qualifications would have required a budget of €1 billion, which seems prohibitive. Overall, these figures are indicative of the difficulty experienced by young NEET people seeking to obtain a driver’s license in France. Assessing the efficacy of the program, our findings regarding employment are mixed. Our results emphasize that driving lessons are intensive, selective, and involve a long-term time frame. Like the case of vocational training, these factors can impinge on investment in both the occupational and non-occupational spheres. Following the analysis drawn from two statistical surveys of young people 12 and 24 months after joining the experiment, the results seem to be largely dominated by lock-in effects. When learning how to drive, young people are less geographically mobile, less active in their search for employment or training courses, and less intent on improving their current employment. However, these findings are reversed after they have passed the test. Two years after joining the program, young people gain in terms of residen-

tial mobility and find temporary jobs more easily, but we still do not find any effect on permanent jobs. Financial support awarded to young people seeking driving lessons therefore has positive effects, but the effects are negative in the first year. Moreover, the presence of negative spillover effects suggests that a generalization of this experiment rendering all young people eligible, which could take the form of a national reduction in the cost of obtaining drivers’ licenses (to take one example), could lead to weaker positive effects on both driving and employment outcomes. To limit this general equilibrium effect, the generalization of assistance when obtaining a driver’s license should be further supported by an increase in the recruitment of examiners, or by the deregulation of examination rules in order to reduce waiting times for theoretical tests, as specified in the Macron Act of 2015. Instead of trying to improve youth mobility by reducing the cost of driver’s licenses, it would be preferable to facilitate youth access to driving lessons and reduce the length and difficulty of the process. Given the magnitude of the lock-in effects, simplifying the driving test according to the model used in many other countries would produce a double dividend by increasing the mobility of young people and facilitating access to employment. Acknowledgments This project has received generous supported from France’s Fonds d’expérimentation pour la jeunesse. An early version of this work was presented at the “Public Policy Assessment” summer school (CNRS Aussois, 2012), the Trajectories, Employment and Public Policy (TEPP) symposium (Caen, 2012), and the 64th Annual Meeting of the French Economic Association (Rennes, 2015). We thank all participants for their comments. We are also grateful for the useful comments of the two reviewers, and from Emmanuel Duguet, Edward Glaeser and David Gray. For their support, we also thank Sophie Kaltenmark, Yiyi Tao and Bénédicte Rouland. We assume full responsibility for any error or flaw contained in this document. Appendix A. The driving license in France and its welfare benefits The cost of driving lessons is substantial in France, as in the UK and northern European countries. By contrast, driving lessons in most US states are fast and simple, while certain countries like Australia, New Zealand and Canada have put in place graduated systems to phase in additional driving privileges. In France, driving lessons involve a long and difficult process for young people and

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driver’s licenses have been made probationary for all new drivers since 2004 (new drivers begin with an initial capital of 6 points but only receive the standard 12 points after a three-years period without losing any points for offences). With 1.7 million tests each year, 1.02 million of which are successful, the driving test is the most frequent examination process in France, and one of the most expensive and difficult for those who take it. Passing the test is especially important for young people with integration difficulties. The process is lengthy, costly and risky, with a final success rate of 60%. The following explains how the French driving test is organized and describes the assistance mechanisms that target the least privileged social groups. The driver’s license in France Obtaining a driving license (Category B) involves the successful completion of two tests, a theoretical test and a practical driving test. To pass the theoretical test, candidates must answer a series of 40 multiple choice questions with fewer than five errors within a time limit. After enrolling at a driving school, it takes an average of four months before the candidate becomes eligible for the theoretical portion of the test. This time frame is set by the administration and depends on the available supply of slots. Candidates who fail this portion must wait at least two weeks before they become eligible once more. After passing the theoretical test, candidates must wait two weeks before taking the practical test. Candidates who do not sign up for the practical driving test within three years, or those who fail to complete it after five attempts, must take the theoretical test again. The practical test involves driving with a licensed examiner for approximately 30 minutes. The examiner assesses compliance with traffic rules, knowledge of the vehicle, the driver’s ability to detect major technical faults, mastery of the controls, handling of the vehicle to avoid creating dangerous situations, ability to ensure his or her own safety and that of others on any type of road, ability to perceive, anticipate and react appropriately to hazards arising from movement, level of autonomy in making a journey, and the ability to drive while respecting the environment and behaving in a civil and considerate manner toward others, especially those who are most vulnerable (Source: Section 1 of Arrêté, February 19, 2010, regarding the practical test for Category B driver’s licenses). Failing the practical test leads to a minimum waiting time of two weeks before the candidate can once again register for an upcoming session. In fact, there are no capacity constraints in France regarding the number of licenses granted every year (this lack of constraints was put in place for taxi drivers, among others). The only limitation stems from examiner availability. In the short-term, there is a fixed number of official examiners (civil servants from the Ministry of Interior), and the higher the number of candidates, the longer the waiting time. This lack of examiner availability means that some candidates may have to wait several months before they can once more take the practical test. They may also be required to take additional, and costly, driving lessons. Since the driving test reform of January 13, 2009, the practical test has been based on the assessment of skills, as opposed to an error report. The success rate exceeded 60% for the first time in July, 2010, compared to 56.6% in late 2008. Welfare benefits for driving lessons There are many welfare programs designed to lower the cost of driving lessons. The central government provides zero-interest loans of €800 to €1200 called “le permis à un euro par jour” (the euro-a-day license). It also contributes to other mechanisms through the Fonds d’Expérimentation pour la Jeunesse. Employment centers offer job seekers financial support of up to €1200, plus €1500 for those on minimum income allowance (RS12 ), using the

12

RSA: Revenu de Solidarité Active.

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personalized welfare-to-work assistance (APRE13 ) to finance all or part of the cost of driving lessons. There are also regional council programs that reduce the cost of driving lessons in 13 of France’s 22 regions. These take the form of a regional tax exemption14 , financial assistance and grants for young and unskilled people. There are also 33 assistance packages offered by area councils (départements) in the form of grants for driving lessons, along with targeted support for young RSA recipients. Finally, 111 city councils also provide means-tested and work program assistance. Among these, 84 municipal councils and five joint municipal councils have adopted a grant system for driving lessons, combined with the euro-a-day program, allowing young people to work for a local authority in exchange for funding for driving lessons. Providing support for driving lessons is a standard practice that includes a wide range of mechanisms funded by all levels of government. Appendix B. The launch of the experiment The “Dix mille permis pour réussir” experiment was launched by the Fonds d’ Expérimentation pour la Jeunesse in the summer of 2009 using a call for tenders aimed at every organization that works with young people with integration difficulties in order to support them for driving lessons. Overall, 58 organizations signed up to the program. These included groups of non-profit youth support centers called missions locales15 (neighbourhood offices), local government authorities that collaborate with the missions locales, and non-profit driving schools. Each project involved a varying number of young people, from a few dozen to several hundred. For evaluation purposes, organizations were grouped by size, with 28 small non-profit organizations of fewer than 100 young people, and 30 large non-profit organizations of 100 young people or more. Among the large non-profit organizations, young people were randomly selected from the test and control groups under a treatment probability of 75%. In some cases, young people were invited to join the program and receive the benefits without taking part in the random draw if an experimenter believed he or she lived under exceptionally difficult circumstances due to their personal history or situation. This “wild card” was subject to strict limitations and justifications. Experimenters were allowed one wild card for every 30 applicant. The non-profit organizations joined the action plan little by little. The larger organizations entered more rapidly and all were effectively in place by June, 2010. By May, 2010, the experiment had welcomed half of its young people. Some of them joined after September 2010, but were omitted from the statistical analysis. By the end of September, 2010, the experiment had welcomed a total of 8121 confirmed applicants. Among those, 7143 went into the random draw, with 5350 (75%) in the test group and 1793 (25%) in the control group. Those omitted from the experiment belonged to the smaller organizations (943), while the wild cards (35) made up only 0.4% of the total number. References Avrillier, P., Hivert, L., Kramarz, F., 2010. Driven out of employment? The impact of the abolition of national service on driving schools and aspiring drivers. Br. J. Ind. Relat. 48 (4), 784–807.

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APRE: Aide Personnalisée au Retour à l’Emploi. In several regions, the applicant must pay a regional tax for the first license application before the exam. The amount of this tax depends on the region. 15 French neighbourhood offices for the social and professional integration of young people (commonly referred to as missions locales) are in charge of providing information and guidance to youths seeking occupational and social integration. Created in 1982, they form a network of more than 450 centres covering the entire national territory. These non-profit organizations are usually chaired by the mayor. 14

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