The Prospect of Legal Status and the Employment Status of. Undocumented Immigrants

Transcription

1 The Prospect of Legal Status and the Employment Status of Undocumented Immigrants Carlo Devillanova, Bocconi University Francesco Fasani, IAE-CSIC, Barcelona GSE, CReAM Tommaso Frattini, University of Milan, LdA, CReAM and IZA PRELIMINARY AND INCOMPLETE. PLEASE DO NOT QUOTE September 2012 Abstract: Illegality of immigration is at the core of the public and policy debate on immigration in many countries. Granting an amnesty is one of the policy option used to reduce stocks of unauthorized immigrants. But, how does the possibility of obtaining legal status affect the employment status of undocumented immigrants? We analyze this aspect in a stylized model where the prospect of becoming legal affects both the reservation wage of the migrant and the value of the match for the employer. In the empirical part, we use a unique dataset which contains daily observations on thousands of undocumented immigrants. We exploit a natural experiment a general amnesty granted in Italy in 2002 which retrospectively set an eligibility rule based on the date of arrival in Italy to develop a DID setup and compare the employment status of undocumented immigrants arrived before and after that date. Our results show that being eligible for legalization positively affects the probability of being in employment after the policy is concluded. The effect is large and statistically significant. The estimates are robust to a number of falsification tests. Our results have important implications for the design of future amnesty programs. Keywords: Illegal Immigration, Amnesty, Regression Discontinuity 1

2 1. Introduction The present paper tries to identify the effect of being eligible for a work-related amnesty on the employment outcomes of undocumented immigrants. Unauthorized immigration is a core policy issue in most developed countries. Nearly 12 million unauthorized immigrants are estimated to reside in the U.S. (Hill et al., 2011). In Europe, the number of undocumented immigrants ranges between 1.9 and 3.8 million individuals, with large variability across countries in terms of incidence over the total population (Kovacheva and Vogel 2009). Current proposals for immigration policy reforms generally include a bundle of complementary strategies which address both the flows of undocumented migrants (i.e. by intensifying border and internal controls, and increasing sanctions) and their stock, through legalization programs. In the recent past, countries have often resorted to amnesties in order to reduce the number of undocumented presences. Probably the most famous legalization episode is the 1986 U.S. Immigration Reform and Control Act (IRCA), which offered a large amnesty program to aliens with sufficient length of residence in the U.S. Amnesties have been frequently run in European countries too. Casarico et al. (2012) examine fourteen European countries in the period and count 18 amnesties, five of which took place in Italy and seven in Spain. Several papers study whether amnesties are an appropriate policy tool to tackle undocumented presences in the country (e.g. Chau 2001; Epstein and Weiss 2011), highlighting the possible effects on the quality of migrants (Karlson and Katz 2003), on future flows of undocumented migrants (Orrenius and Zavodny 2003), on the labour market outcomes of natives and previous immigrants (Cobb-Clark et al. 1993), on public revenues and expenditures (see Orrenius and Zavodny 2012 for an up-to-date review) 1. One major line of research tries to estimate the effect of amnesty on the labour market outcomes on newly legalized immigrants, including wages, employment and 1 On policies to reduce illegal entry of immigrants or legalize illegal immigrants see also Ethier (1986), Chiswick (1988), Hanson and Spilimbergo (1999), Hanson et al.( 2002), Woodland and Yoshida (2006), Facchini and Testa (2011). Hanson (2006) provides a recent review of the literature on illegal migration from Mexico to the United States. 2

3 participation decision 2 (e.g. Amuedo-Dorantes et al. 2007; Amuedo-Dorantes and Mazzolari, 2010; Amuedo-Dorantes and Bansak 2011; Barcellos 2011; Borjas and Tienda 1993; Cobb-Clark et al 1995; Lozano and Sorensen 2011; Kaushal 2006; Kossoudji and Cobb-Clark 2002; Rivera-Batiz 1999; Singer 1994). The received literature highlights several theoretical channels trough which legalization may affect the labour market outcomes of immigrants, including better employeremployee match (because, for example, of increased geographical and occupational mobility, reduced risk in job-search activity, availability of formal recruiting channels), higher bargaining power, the eligibility for social programs (e.g. Rivera-Batiz 1999; Amuedo-Dorantes and Bansak 2011). The theoretical predictions are that legalization should unambiguously increase wages (and/or returns to skills) for those immigrants who were employed before the amnesty and continue to be employed after legalization. The effect of an amnesty on individual s labour supply depends on the on the size of income and substitution effects, and the generosity of the welfare system. The main challenge of this empirical literature is an estimation of these effects which take into account the selection into legal status (i.e. migrants are not randomly assigned to legal status). The identification exploits the variation in legal status induced by amnesty, and compares the outcomes of newly legalized immigrants to that of a suitable control group. For example, in their early study Borjas and Tienda (1993) use administrative data on legalized immigrants and compare their labour market outcomes with those of the foreign-born population from CPS; Kossoudji and Cobb-Clark (2002) use as a comparison group all legal Latino men, natives as well immigrants; a similar approach has been adopted by Amuedo-Dorantes and Bansak (2011), whose control group is made by a subsample of Hispanic natives. Most studies look at the effect of 1986 IRCA, which designed a mixture of strategies to deal with undocumented immigration, including employer sanctions for hiring undocumented workers. This makes it hard to disentangle the effect of the amnesty from the other policy changes (Kaushal, 2006). Kaushal (2006) studies the effect of 1997 Nicaraguan 2 A related strand of the literature looks at the effect of naturalization on current behavior of immigrants, focusing on labour market outcomes (Bevelander and Pendakur 2012). Mazzolari 2009), fertility and health of immigrants children (Avitabile et al. 2012) and integration (Avitabile et al. 2010). 3

4 Adjustment and central American Relief Act (NACRA). The author adopts a DID approach in which the treated group is made of noncitizen men eligible for amnesty under the Act, and the control group is made of (similar in terms of length of stay) noncitizen men from other countries of Latin America. Orrenius et al. (2012) exploit the 1992 US Chinese Student Protection Act (CSPA). In their DID regression the treatment group is immigrants from mainland China, and the control groups are immigrants from Hong Kong, Taiwan, or Korea, who were not eligible for CSPA. Despite the variety of approaches used in the literature, in general results show that the legal status is associated to higher wages, wage growth and returns to human capital. The empirical studies still do not resolve the theoretical ambiguity of the effect of amnesty on employment and participation. For instance, Amuedo-Dorantes et al. (2007 and 2011) find that newly legalized workers experience lower employment for both male and female, which results in a higher unemployment for male and a lower participation rate for women; the effect on employment is found to be statistically insignificant in Kaushal (2006) and even positive for female immigrants (Pan 2010). The present paper is part of (and tries to contribute to) that line of research that aims at quantifying the effect of amnesty on the labour market outcomes of migrants. In this respect, it is strictly linked to the above studies. However, we depart from existing literature in two key aspects. First, we focus on the effect of being eligible for amnesty on the employment outcomes of undocumented workers, while previous studies have addressed the impact of gaining legal status (or naturalization) on some immigrants outcome or behaviour. This point is crucial and it merits comment. By now, the literature has looked at the impact of being granted legal status, comparing labour market outcomes of immigrants non-eligible for an amnesty with those of the immigrants who were legalized. The non-eligible undocumented immigrants are out of the picture, mainly because of data limitations. On the contrary, the immigrants in our sample are all undocumented and they are still undocumented when we measure their employment status (see Section 3 for a description of the data). Some of them, though, are eligible for applying for legal status and some of them are not. We exploit a natural experiment a general amnesty granted in Italy in 2002 which 4

5 retrospectively set an eligibility rule based on the date of arrival in Italy to develop a DID setup and compare the employment status of undocumented immigrants arrived before and after that date. The discontinuity introduced by the 2002 amnesty plus the uniqueness of our dataset provide us with the ideal comparison group: (...) a randomly selected group of undocumented immigrants similar to the target group, but ineligible for, and unaffected by, amnesty (Kaushal 2006 page 635). One further advantage of focusing on undocumented immigrants is that we are able to identify a new mechanism linking amnesty to employment outcomes, that has never been explored before. We highlight the fact that one could observe changes taking place in the labour market even before the actual legalization occurs. We think that the employment response which occurs when an undocumented immigrant becomes potentially eligible for an amnesty can be crucial in order to have a complete picture of the whole employment effects of legalization, which adds up those addressed in the present paper plus those studied by previous research. The main shortcoming is that it is difficult to contrast the results of our analysis with that of all the other existing studies. The second major departure from existing studies is that we look at the effect of a specific type of amnesty, that conditions the eligibility for legalization to being employed in the country at the date of the application. Work-related amnesties are not an exception. For instance, most of the amnesties (2004, 2001, 1991, 1985) launched in Spain in between 1985 and 2004, the 1991 amnesty in the Netherlands, and the 2006 Italian amnesty were targeted to workers in the country (Casarico et al. 2012); IRCA had a Special Agricultural Worker (SAW) program granting amnesty to illegal workers in agriculture as well. Furthermore, many countries are implementing work-related visa schemes (often temporary), which might have similar effects 3 and, in some case, work as de facto work-related amnesties, if the country fails to enforce the migration controls. This is certainly the case for Italy. Italy implements a migration quota agreement Decreto Flussi, which annually sets 3 To the best of our knowledge, the only available evidence is on wages in the US. Mukhopadhyay and Oxborrow (2012) find that the temporary workers (i.e. the ones without a green card) earn less than comparable immigrants with a green card. Their result suggests that the current process of acquiring green card gives too much power to employers and hinders job mobility among high skill immigrants. 5

6 the maximum number of non-eu foreigners who can be allowed to come and work in the country. In theory, to be admitted within the quota system, the worker has to reside outside Italy: if an employer wants to hire a non-eu worker, and he/she already knows the worker, he/she must submit a personal application for work authorisation. If the work authorisation is accepted, the worker must come to Italy within a fixed period of time and regularize his/her position. In practice, however, there is plenty of evidence that the system is used by the employers to legalize undocumented workers already in the country. In the following theoretical Section 2 we argue that the employment requirement may have an effect both on the demand and on the supply of undocumented labour 4, resulting in higher employment rates of undocumented immigrants, possibly via a reduction of their reservation wage. In our empirical analysis, we estimate the overall increase in employment due to the eligibility for amnesty, but we are not able to disentangle the demand and the supply effect. We find that... TO BE COMPLETED 2. Theoretical framework This section presents a theoretical framework to elucidate the effect of a work-related amnesty on the employment rate of eligible undocumented migrants. It is worth stressing that none of the channels highlighted in previous studies apply to our setting. In fact, this paper looks at the effect of being eligible for the 2002 work-related amnesty on the employment outcomes of undocumented immigrants. Therefore, individuals in the treated and the control group do not differ in terms of legal status. It is also worth mentioning that in Italy undocumented immigrants are precluded from accessing welfare benefits, except for few specific health care programs 5. Moreover, since the availability of private resources is likely to be scarce too, their labour supply is very inelastic and, having no form of employment protection, their bargaining power is low. 4 We stress once more that we are dealing only with undocumented immigrants: the choice for the employer, therefore, is not between a legal or an illegal immigrants, but between two illegal immigrants, of whose one is eligible for amnesty and the other not. 5 These are: emergency and preventive care, treatments related to communicable disease, pregnancy and childbirth. 6

7 The model is intentionally very simple and it only aims at shedding some light on the relations studied in the empirical part of this paper. The main point of this section is that being eligible for a work-related amnesty increases the room for a profitable job-match between the (undocumented) worker and the firm, because both of them anticipate the reduction of the expected penalty. The model abstracts from general equilibrium considerations and it is static. Notice that in the absence of firing costs and significant on-the-job training, it seems appropriate to assume that the firm s decision on whether to employ a undocumented worker is static. To focus on essentials, we also assume linearity of the production function in the only factor, labour. Consider the choice of an undocumented immigrant, who has to decide whether to accept a job offer or to reject it. He/she decides to accept the offer if: e u u (1 p) w p c (1 p) b p c (1) where e u w is the wage of a successful employee-job match, ( 0) c is the penalty for being apprehended, b( 0) is the opportunity cost of not working and p and p denote the probability of been apprehended for, respectively, employed and unemployed individuals. The relationship between p and p is likely to vary across occupations. For instance, it is reasonable to assume p p in domestic occupations, for which on the job controls are more difficult to be implemented; on the contrary, being employed in construction and services might even increase the risk of detection, suggesting p p. The model distinguishes between the probability of apprehension for employed and unemployed individuals because of the specific eligibility rules for legalization that characterize the amnesty studied in this paper. In fact, eligibility was conditioned to the date of arrival in Italy and to being employed in the country at the date of the application. It follows that p u and c ( 0) have not been affected by the amnesty, whereas p has. Setting b (1 p) b p c and solving for the reservation wage of the worker u w we get: u u u p c b w (1 p) 7 (2)

8 u The reservation wage w ( p ) is increasing in the probability of being detected, with u w b if p 0 and lim w p 1 u. Note that for u c (b ) high (low) enough, b 0 and a negative reservation wage cannot be excluded. One further property of equation (2) is that if p reduces to u w b and a change in the probability of apprehension has no effect on it 6. p the reservation wage Consider in turn the problem of a firm f, which has to decide whether to make a job offer or not. As already stressed, the choice is not whether to employ a documented or an undocumented worker, as all individuals are undocumented in the model. The firm decides to offer a vacancy by comparing the expected revenues to the cost of employing one more worker. It opens a vacancy if and only if: f e (1 p) A p c w (3) f where A( 0) is the marginal productivity of the worker, c ( 0) the associated sanction for the firm. For the firm, the only relevant probability of apprehension is p, which for simplicity is the same faced by the undocumented worker. Equation (4) defines the maximum wage f w that the firm is willing to pay to employ an undocumented worker. f f w (1 p) A p c (4) f w ( p ) is linearly decreasing in p. For p 0 (zero probability of detecting the undocumented worker), the maximum wage that the firm is willing to pay equals the worker s marginal productivity A. For p 0 the firm takes into account that with a positive probability the match will be broken and, in this case, it incurs in the sanction If the marginal productivity of the match is higher than the individual s utility of not working (i.e. if A b) 7, equations (4) and (2) define p such that f u w ( p) w ( p). For p p, f u w ( p) w ( p) and f c. 6 In the most general case where p p( p), with u dp( p) 0 dp, the sign of dw ( p) dp unless imposing further restrictions on the parameters of the model. 7 This condition is always satisfied if b=0. 8 cannot be univocally determined,

9 the two curves identify a region in the j w p space (j = f, u, e) in which, for any w e ( w f, w u ), the firm is willing to employ the undocumented immigrant and the worker is willing to accept the job f u f offer. The slope of the w ( p) and w ( p ) curves also implies that the distance between w and w is decreasing in p: f u d w ( p) w ( p) 0 (5) dp On the contrary, to the right of p we observe u f w ( p) w ( p) and there is no possibility of a mutually profitable match. u To close the model, we assume that, for p p, the probability that the match occurs is an increasing function of the surplus w f u w : u f u ' prob( employment ) g( w w ), with g ( ) 0 (6) j where, for simplicity, we have suppressed the argument of the w () functions. In words, the higher the wage the firm is willing to pay, relative to the minimum wage acceptable by the worker, the higher the probability of a successful match. Equation (6) can be interpreted as the result of a matching process, in which the firm searches for a worker and the worker searches for a job: the higher the potential surplus of a successful match, the higher the probability that it occurs. This can be justified by the greater search intensity of either the firm or the worker, or the larger room for an agreement on the actual wage to be reached. If a successful match occurs, the wage can be any w e ( w u, w f ), depending on the bargaining power of the firm and the worker. Imagine, now, that there are two types of undocumented workers, those eligible (u,e) for an amnesty and those who are not (u,i), with 0 u, e u, i p p p. Condition p p crudely captures u, e u, i in our static set-up the higher expectation of being apprehended of individuals ineligible for the amnesty. Notice that being eligible for the amnesty does not affect the left hand side of equation (1), as it only modifies the probability of being regularized conditional on being employed. 0 p ue, 9

10 makes it clear that eligible individuals are still undocumented in the country and it allows for unsuccessful applications to the amnesty. Eventually, eligible workers are going to gain legal status and condition (2) is not pertinent any more. From (5) and (6) it is straightforward to conclude that prob employment u, e u, i ( ) prob( employment ) (7) and, ceteris paribus, the employment rate should be higher among those undocumented migrants which are eligible for the amnesty, relative to those who are not. This testable implication is confronted with the data in the following empirical analysis. This conclusion should hold a fortiori in a more sophisticated set-up, where individuals attach a positive value to gaining legal status per se, that is, beside the labour market premium here modelled. Note that condition (7) is driven by both the firm s higher willingness to pay for an eligible worker and the worker s lower reservation wage. The following empirical analysis is unable to disentangle f u the two effects, whose relative magnitude depends on the slope of the w ( p) and w ( p ) curves. It can be argued that the bargaining power of undocumented workers is low, which would imply an equilibrium wage dw dp e e u w w and 0. A strictly related issue is that, since workers bargaining power depends on their legal status, the equilibrium wage e w could itself be a function of the probability of being apprehended w u p w e ( p) w f p, where both the extremes of the target set u f w and e w and the equilibrium wage w () are a function of p, with e dw dp p 0 i.e. the lower the apprehension probability, the higher the worker s bargaining power and the resulting equilibrium wage. Brown et al. (2009) show that firms employing undocumented workers may enjoy a competitive advantage over firms that do not employ undocumented workers, probably because of monopsonistic discrimination against them. This consideration could affect the main testable implication of equation (7) if, in an extended model, firms were allowed to select workers 10

11 according to their legal status. In this case, firms, anticipating the higher bargaining power of newly legalized workers, might prefer not to employ them and condition (7) could be violated. In our model, a sufficient condition to exclude this result is that in the right neighbour of p 0 (the status of documented immigrant) the wage reduction induced by an increase of the apprehension probability is low enough i.e. dw e dp p p 0 f A c. We can speculate that this condition is likely to be satisfied since the Italian legislation in 2002 linked the maintenance of the legal status in the future to a strict employment requirement which gives strong bargaining power to the e employer. Note, however, that none of the above conjectures on the shape of the w () function can be tested here, because our data have no information on wages. 3. Empirical strategy a. A natural experiment: the 2002 Italian Amnesty We are interested in estimating the effect of having the possibility of receiving legal status on current employment rate of undocumented immigrants. According to our theoretical model, we expect a change in the likelihood of being granted legal status in the future to produce effects on both labour demand and supply. Does the future prospect of being legalized increase the employability of undocumented immigrants (i.e. increasing labour demand)? Does it shift their labour supply? We address these questions exploiting a unique experimental setting provided by a general amnesty granted in Italy in The amnesty, which was deliberated by the Italian government on the 9 th of September 2002 and became effective the following day, granted legal status to all undocumented immigrants who satisfied two eligibility criteria, and filed an amnesty application within the 11

12 deadline of the 13 th of November The eligibility criteria were: a) being in Italy for at least three months on the day the amnesty started (i.e. being in Italy since the 11th of June 2002), b) having an employer willing to hire the applicant (with a fully legal contract). Applying for the amnesty also required the payment of a fee, equivalent to three months of social security contributions. The timing of the amnesty is sketched in Figure 1. [Figure 1 approximately here] The amnesty was deliberated after over a year of discussion within the government, which was extensively covered in the media (see appendix???). Moreover, the frequency and regularity of general amnesties granted in Italy (in 1982, 1986, 1990, 1995 and 1998) possibly create the expectations among immigrants that a new amnesty will be offered after two-three years from the last one. Both aspects make it very likely that a significant fraction of the undocumented immigrants arriving in Italy in the months before the amnesty was actually voted were hoping to get legal status through a new amnesty. Nevertheless, for our identification strategy, the crucial aspect of this policy is that it set a retrospective minimum period of permanence in Italy, which created an eligibility threshold (the 11th of June 2002) that was ex-ante unpredictable. Therefore, even if the arrival of all undocumented newcomers were motivated by the expectation of the amnesty, the arbitrariness and unpredictability of the eligibility threshold day implies that there are no reasons to expect significant differences in (observable and unobservable) characteristics between immigrants arrived immediately before and after June 11 th. Our identification design exploits the exogeneity in assignment of the eligibility condition based on arrival in Italy (condition (a) above), which is predetermined at the time the amnesty is deliberated and made public. The second eligibility condition (condition (b)), instead, which refers to the employment status of the migrant after the amnesty is opened, cannot be regarded as exogenous because being employed is the outcome of a process involving endogenous individual decisions. Indeed, our outcome of interest will be the employment status of undocumented immigrants. One 12

13 way of interpreting our findings is to assess the extent to which fulfilling the arrival date requirement affects the probability of fulfilling the second requirement too. b. Estimating equation Since our aim is to estimate the causal effect of the prospect of obtaining legal status on employment probability, we would like to run a regression of the form: empl i EL X u (3.1) i i i where empl is a dummy variable which takes value 1 if individual i is employed, and 0 otherwise; EL is a dummy variable equal to 1 if the undocumented migrant is eligible to apply for legal status, and value 0 if she is not; X is a vector of individual control variables; and, finally, u is an idiosyncratic shock. The coefficient indicates in this case the difference in employment probability between eligible and non-eligible undocumented immigrants. The ideal experiment which would deliver a causal interpretation of the coefficient is a setting where one can observe a population of undocumented immigrants, and a random subsample of this population is given the possibility of obtaining legal status in the future, while the others are not. Clearly, such an experiment can hardly be run in practice. In our analysis we exploit the design of the 2002 immigration amnesty in Italy which, as explained in section 3.a, contained an eligibility criterion based on the date of arrival in Italy. The discontinuity introduced by the retrospective choice of an arrival date for eligibility creates local randomness in eligibility status and naturally defines a treatment and a control group, which consist of immigrants arrived just before or just after the eligibility date. The empirical exercise will then consist in comparing the outcomes of the two groups when the amnesty deadline expires, i.e. before their applications are processed and successful applicants receive their working visa. In this way we will be comparing the employment status of two groups of undocumented migrants who only differ with regard to their possibility of 13

14 obtaining legal status. This exercise is valid as long as the eligibility criteria are orthogonal to individual observable and unobservable characteristics. We therefore start by estimating linear probability models of the form in (3.1), using observations on employment status of undocumented immigrants collected between the 14 th of November and the 13 th of December 2002, that is in the thirty days following the deadline of the amnesty. However, as we explain in section 3.d, data constraints force us to choose in our baseline regressions two months intervals before and after the threshold date to construct the treatment and the control group. Therefore on the amnesty closing day individuals in the treatment group have spent in Italy up to five more months than those in the treated group. Since a key determinant of immigrants labour market integration is the time spent in the host country one may fear that differences in employment probability between the two groups might simply reflect differences in migration seniority, rather than differences in eligibility status. To check for this possibility, we proceed in two ways. First, we perform some placebo tests running regressions of the form in (3.1) for years 2000, 2001 and 2003, when no amnesty was in place. Second, we pool all years and perform a fully-fledged differences-in differences analysis running regressions of the form on data for the period November 14 th -December 13 th in every year: empl i Y2002 EL 3 EL Y2002 X u 1 i 2 i i i i i (3.2) where Y2002 is a dummy variable indicating the year of the amnesty, and captures all labour market features specific to the amnesty year which affect both eligible and non-eligible immigrants; EL is a dummy variable indicating immigrants arrived before June (see section 3.d for details) which captures any systematic difference in employment probability between the two groups. Our coefficient of interest is β 3, which measures the difference in employment probability between immigrants who have the possibility of applying for the amnesty and the other undocumented immigrants. 14

15 c. Data The present study uses a unique dataset collected by Naga, a voluntary association which offers free primary care to irregular immigrants. Naga is a large organization, supplying a daily average of over 60 visits, 5 days a week. Being located in Milan, its services are used by residents of the city or of its close suburbs. The association does not discriminate immigrants in any way according to their nationality and/or religion. There is no eligibility issue. If a regular immigrant reaches Naga, she/he is redirected to the National Health Service and therefore the sample does not include regular immigrants. In order to facilitate the doctors tasks, Naga volunteers carry out short interviews with the immigrants during their first visit completing a file with personal information. The information available on electronic format was collected since year 2000 and contains a snapshot description of the immigrant s social and economic situation at the time of the visit. It includes: country of origin, sex, date of birth, date of arrival in Italy, date of visit, marital status, number of children, education, current employment, occupation in the home country, knowledge of Italian, accommodation, and Naga contact (who introduced him/her to Naga). An earlier version of this dataset has been used in Devillanova (2008). In our analysis, we focus on the working age population (16-65) only. The main shortcoming of the dataset is that it is a non-random sample of irregular immigrants, as it includes only individuals that choose to visit Naga for medical care, and several factors influence this event. In particular, individuals of a lower socio-economic status may be over-represented for a number of reasons. The most obvious one is that individuals must be seeking health assistance, which, in turn, is clearly linked to their socioeconomic conditions. Second, poor immigrants cannot afford the cost of a private doctor and, therefore, their only chance of getting primary medical care is through Naga, or other voluntary associations. Finally, Naga is open only during working hours, limiting the possibility for employed immigrants to take advantage of the service (notice, in addition, that being sick could prevent individuals from working). Overall, these factors tend to select immigrants in the sample according to their income (poorer) and employment status (jobless). 15

16 Further selection into Naga can originate from cultural factors (in particular trust in Western medicine as compared to other styles of remedies) and from the characteristics of the migratory pattern (well established communities might provide their members with alternative resources and services to deal with health needs, but also with more information about Naga). We try to address these issues in the regression analysis by controlling for individual and country specific characteristics. Note however that any issue of sample selection would be in our case common to both the eligible and the non-eligible population. d. Construction of treatment and control groups and sample extraction While ideally we would compare the employment outcomes of immigrants arrived in Italy in the week before (eligible for the amnesty) and the week after (non-eligible for the amnesty) June 11 th, two data limitations do not allow us to do so. First, we have no information on the exact date of arrival in Italy, but we only know the month and year of arrival. Second, because of the small sample size, even if we had precise information on the arrival date, we would still have to select a wide time interval to have a sufficient number of observations. In our baseline specification, we define as eligible (treated) all immigrants who arrived between April and May 2002, and as control group we use all immigrants arrived in Italy between July and August We exclude from the sample all individuals who arrived in Italy in June 2012 as we are unable to determine whether they meet or not the eligibility criteria (i.e. whether they arrived before or after the 11 th of June). We have summarised the timing of the amnesty and the definitions of the treatment and control group in Figure 2. [Figure 2 approximately here] Since we want to study how the prospect of obtaining legal status affects the employment probability of undocumented immigrants, in our analysis we would like to compare the employment 8 As a robustness check, we have also restricted the time interval to one month. See section 4. 16

17 outcomes of the treatment and control group on the amnesty deadline day, or in the few days just after the deadline. In this way the positive effects of the prospect of obtaining legal status due to the amnesty have already developed, but even eligible applicants are still effectively undocumented. The further we move away from the amnesty deadline day, the more likely it is instead that successful applicants leave our sample, as they have become legal and as such entitled to free medical care from the National Health Service. The undocumented immigrants arrived before June 2002 and observed at Naga long after the amnesty deadline will therefore be a negatively selected sample of their arrival cohort. Since the daily number of observations is small, we cannot limit our attention to the amnesty deadline day, or the week immediately following the day. Rather, in our baseline analysis we will observe the employment status of immigrants in the 30 days following the amnesty deadline day, i.e. from the 14 th of November to the 13 th of December Finally, we also extract the same sample for years 2000, 2001 and 2003 and use them as placebos. Summing up, our main sample contains observations for the period November, 14 December 13 of years 2000, 2001, 2002 and 2003, and is formed exclusively of undocumented immigrants arrived in Italy in April, May, July or August of the same year in which they are observed. It consists of a total of 272 observations. In Table 1 we report some descriptive statistics of our sample, for each year and by treatment status. This also serves as a test of the randomness of the treatment status. [Table 1 approximately here] The table shows that in 2002 over 50% of the sample is composed of men, and that the average age is just above 29. The average education is high: over 40% of the sample has attended high school, while about 10% has some university education. The differences between the treatment and the control group in these variables are never statistically significant at 5%. In terms of areas of origin, instead, the composition is slightly different between the treated group, where Latin America is the largest single area of origin, and the control group, where Eastern Europeans represent the largest origin group. The treatment and control group in 2002 are therefore similar with respect to all 17

18 characteristics, except for their countries of origin composition. The remaining columns report the same descriptive statistics for the placebo years, and show a similar pattern. 4. Results Regression discontinuity We start by estimating regression equations of the form in (3.1), where we define as eligible (EL=1) migrants arrived in April and May, and as non-eligible migrants arrived in July and August, and we observe their employment status between the 13 th of November and the 13 th of December. We account for the heteroskedasticity generated by the choice of a linear probability model using robust standard errors. Regression results are summarised in Table 2, where we report the estimates of obtained in 2002 (row1), and in the three placebo years 2003 (row 2), 2001 (row 3) and 2000 (row 4). [Table 2 approximately here] In column 1 we report the estimates from a specification which includes no control variables: the results of row 1 show that immigrants who were eligible to apply for the amnesty are over 30 percentage points more likely to be employed than non-eligibles. Are these results driven by differences in observable characteristics between the treated and the untreated groups? Although we have shown in Table 1 that the two groups are similar in terms of their observable characteristics, in columns 2 to 5 we progressively include control variables to account for differences in composition. In column 2 we report results from a regression where we include a gender dummy, dummies for five-year age groups and dummies for four education levels (no education or primary education, secondary education, high school, university education). The estimated coefficient reduces only slightly, from to In column 3 we additionally control for differences in areas of origin 18

19 (which we highlighted in Table 1), including dummy variables for five macro-areas of origin (Europe, Asia, North Africa, Sub-Saharan Africa and Latin America): the difference in employment probability persists, although it decreases a little to In column 4 we include month dummy variables that capture potential seasonality effects in employment status: again, their inclusion affects the estimates only marginally, pushing the estimated gap up again to Finally, in column 5 we take advantage of the information on immigrants occupation and labour market status in their country of origin, which may capture other dimensions of human capital and labour market experience that have not been controlled for yet. We control for labour market background in the home country by including dummy variables for each of the eleven home-country occupational or employment status category values. Since the variable on occupation is missing for over 17% of the sample, we also keep these individuals in the sample and include a dummy for missing. Due to the small sample size, the inclusion of these dummies considerably saturates the model; nevertheless, our estimated coefficient is still positive and significant at 5%, and its size is in line with previous estimates at Results of row 1 demonstrate clearly that the employment probability of treated immigrants are significantly higher than those in the control group. Is this difference due to their difference in eligibility for the amnesty? Or are there any characteristics of undocumented immigrants arrived in April-May which make them more likely to have a job in November than immigrants arrived in July and August? To address these questions, we replicate our base regressions (3.1) for the placebo years 2003, 2001 and 2000, when no immigration amnesty was in place. Any significant differences in employment probability between the two groups of immigrants in a placebo year would be an indication that other factors, like for instance the difference in time spent in Italy, may be responsible for the employment differential we have shown in year The results of rows 2-4 show that employment probability differences between the placebo treatment and the placebo control groups are close to zero or negative, but never statistically significant in any year. The absence of any significant employment advantage for immigrants 19

20 arrived in Italy in April and May relative to those arrived in July and August in non-amnesty years is a strong indication that the results for year 2002 are indeed driven by the difference in amnesty eligibility and not by other factors. The annual sample size in all the regressions shown above is small, in particular in some years. As a robustness check on our results we therefore have also replicated the previous analysis extending the observation window to the two-months interval after the amnesty deadline, i.e. from the 14 th of November to the 13 th of January. As we explain in section 3.d the extension of the observation window further from the amnesty closing day may tend to select negatively on employment the eligible immigrants who are still in the sample. This will work against finding any employment differential between eligible and non-eligible immigrants. On the other hand, it allows us to increase the number of observations, and thus to obtain more precise measurements. Results from this robustness check, reported in the bottom panel of Table 2, confirm our main findings. As expected, though, the estimated employment differential between eligible and non-eligible immigrants is reduced. We still find no significant differences in employment probability between the two groups in the placebo years. Difference in differences While in Table 2 we have run separate regressions for the amnesty and the placebo years, in this section we develop a fully-fledged diff-in-diff strategy (see section 3.b), and run regressions of the form in (3.2). We start by using all available years, Therefore, we will be comparing the employment probability of undocumented immigrants arrived in Italy in April and May 2002 to the employment probability of undocumented immigrants arrived in Italy in July and August 2002, as well as to that of undocumented immigrants arrived in Italy in April and May of years 2000, 2001 and The first row of Table 3 reports the estimate of the coefficient β 3 in this case. [Table 3 approximately here] 20

21 As before, we start in column 1 from a specification without control variables, and we increasingly add controls in the columns to the right. The estimated coefficient is positive, strongly significant, and remarkably stable across specifications, ranging between and The results of column 5, where we control for gender, age, education, area of origin, month of observation, and profession in the country of origin indicate that the prospect of obtaining legal status increases the employment probability of undocumented immigrants by 31.2 percentage points. In rows 2 to 5 of Table 3 we check whether the results are sensitive to the choice of the control years. In row 2 we use the year before and the year after the amnesty (2000 and 2001) as control groups, in row 3 the control group is formed by the two years before the amnesty (2000 and 2001), while in rows 4 and 5 we compare the amnesty year separately to the year after (2003) and the year before (2001), respectively. The magnitude of the estimated coefficient changes slightly according to the control year chosen, but it always indicates an employment probability advantage of about 30 to 40 percentage points for immigrants eligible for the amnesty. Robustness checks We have conducted several test to check the robustness of our results. First, we adopt a narrower definition of the eligible and non-eligible group, using a one month interval (rather than the current two months) around the eligibility threshold date. We therefore limit our attention to individuals arrived in May (eligible) and in July (non-eligible). This has the advantage of considering individuals in a smaller interval of time around the discontinuity, and hence strengthening the assumption of randomness in eligibility status, but comes at the cost of decreasing the number of observations in our sample. We show results from regressions where we use this narrower definition in row 6 of Table 3. Although the number of observations in this case is less than half those with the original sample definition, the estimated coefficients are still positive and precisely measured. The estimated effect tends to be even larger than the one estimated in our base regressions. Note that the estimate reported in column 5 is not statistically significant at the 21

22 10% level, although the size of the coefficient is in line with estimates from other specifications. This happens because the specification in column 5 is highly saturated, with plenty of dummy variables that capture most of the variability in the data. Nevertheless, the p-value for this coefficient is just above 12%. In our second robustness check we extend the observation window after the amnesty deadline to 60 days, in a similar fashion to the robustness check we have performed on our base RD results. We report results from regressions using this wider observation window in row 7 of Table 3. The estimated difference in employment probability is still positive and statistically well determined in all specifications, although smaller in size, as expected, at about 0.2. Finally, we have also performed a placebo analysis. We exclude year 2002 from the sample, and run regressions of the form in (3.2) where we replace the dummy variable Y2002 with, alternatively, dummy variables for years 2000, 2001 and Since no amnesty was in place in any of these three years we should not find any significant estimate of β 3 in these regressions. [Table 4 approximately here] Indeed, the results from all placebo regressions, reported in Table 4, show no significant effect of the placebo amnesty in any year. In Table A1 in the Appendix we have also replicated all the placebo regressions displayed in Table 4 using a one month interval around the threshold date (i.e. using only individuals arrived in May ( eligible ) or in June ( non-eligible ). Again, as expected we do not find any significant result. 5. Dynamic effects So far we have observed our treatment and control groups after the amnesty deadline, and we have shown that undocumented immigrants who have the prospect of obtaining legal status are more likely than non-eligible immigrants to have a job. In this section we take a more dynamic approach, and study how the employment probability differential evolves over time. As we explain in section 3.a, the amnesty was passed on September 10 th On that day it was also announced that only 22

23 immigrants arrived before the 10 th of June 2002 would have been eligible to apply. Therefore, until the 10 th of September eligible and non-eligible immigrants were undistinguishable, and the employment probability of those arrived before and after the 10 th of June should thus be the same, if the two groups are not different (which is our identifying condition). Once the amnesty is approved, however, and until its deadline on the 13 th of November, the two groups become clearly distinguishable, and we expect their employment rates to gradually diverge over the two months period between the 11 th of September and the 13 th of November This is what we show in Table 5, where we have replicated the DiD approach of equation (3.2) to study the evolution of the employment probability differentials between eligible and non-eligible immigrants over the course of the amnesty period. [Table 5 approximately here] In the top panel of the table we analyse the first month after the opening of the amnesty (September 11 to October 10), while in the bottom panel we repeat the analysis for the second and last month of the amnesty (October 11 to November 12). The results are coherent with our theoretical expectations. In the first month after the opening of the amnesty, the employment rates of eligible and non-eligible immigrants are not statistically significant in any specifications, and regardless of the control years adopted. However, after the amnesty has been in place for a month, and as we approach the deadline, the employment rates of the two groups start to diverge. Eligible immigrants have an employment probability that is about 20 percentage points higher than for non-eligibles, even though the effect is not precisely measured in all specifications. In Table A2 in the Appendix we have replicated the same analysis using the narrower (one month) definition of eligible and noneligible groups. Results in that table show that when we focus on immigrants arrived in May and June only, and despite the fact that the sample size is considerably smaller, the same pattern of results is clear, and the improvement in the second half of the amnesty period is even more precisely measured. 23