In the absence of any employment friction, any temporary immigrant worker should receive the same wage as an equivalent (i.e., other things being equal) native worker. If the wage offered by the current employer is below the worker’s marginal productivity, another employer can potentially poach the worker and still earn a profit. The structure of immigration rules creates friction in the labor market that may prevent temporary workers from earning the same wage as natives and permanent residents. There are two potential sources of friction (Gass-Kandilov 2007). One such source of friction is the direct cost of legal and processing fees, which total about $6,000 (NFAP 2006). But the primary source of this friction is the restricted mobility among immigrants during the period between applying for permanent residency and receiving permanent residency (i.e., green card). Because the number of temporary worker visas is far greater than number of work-based permanent visas issued each year, a large number of temporary workers have to wait a substantial length of time, roughly 6 to 10 years (NFAP 2009), for their permanent-residence request to be processed. Although most H-1B holders would like to have a green card (Wayne 2001), it is not possible to determine exactly how many H-1B holders eventually get a green card because the Immigration and Naturalization Service (INS; now known as the U.S. Citizenship and Immigration Services or USCIS) kept no statistics on the number of H-1B’s who eventually receive green cards (Wayne 2001). The percentage of successful transfers from a temporary H-1B worker to a legal permanent resident remained undocumented by the INS until its dissolution in 2003 (Wayne 2001). By using data from the U.S. Citizenship and Immigration Services (USCIS) and the U.S. Department of Homeland Security (DHS), however, we can get a rough estimate on the upper bound. For example, column 1 of Table 1 shows the number of new H-1B petitions approved during the years 1999–2005. The average number of H-1B petitions approved during this period was 129,877 per year. Column 2 shows the number of EB legal permanent residencies (LPRs) awarded to adjustees in the same period, with the average being 54,688. Given the delay in processing LPRs, these averages are not directly comparable. To make the numbers roughly comparable, we focus on the average of the number of H-1B petitions approved during the years 1999–2001 (about 150,000) and the average number of EB green cards awarded to adjustees in 2004–2005 (about 84,000), thereby allowing for a five-year delay in the reception of the LPR status. The ratio of the number of EB LPRs granted to adjustees to the number of H-1B petitions approved is about 56%. This is an approximate upper bound; the true estimate of the share of H-1B workers that end up with a green card is even lower than 56% because some of the immigrants who were awarded EB green cards may have entered the country on L-1 or other visas. While these immigrants wait to become permanent residents, they are unable to change jobs without losing their position in the visa queue or, in many cases, even to accept a promotion (because green card applications cannot be transferred) without losing their position in the visa queue. The restrictions of the application procedure may lead employers to underpay their foreign workers because of immigrants’ highly limited mobility. Although employers are legally required to pay the “prevailing wage” to H-1B employees, opponents of such programs argue that existing loopholes may cause employers to underpay their immigrant workforce (Hamm and Herbst 2009; Matloff 2004). A study conducted by the U.S. General Accounting Office (2003:1) reported that “Although some employers acknowledged that H-1B workers might work for lower wages than their U.S. counterparts, the extent to which wage is a factor in employment decisions is unknown.” Furthermore, L-1 visas do not require employers to pay the prevailing wage to workers (Zavodny 2003). Gass-Kandilov’s (2007) is the only study (that we are aware of) that used individual-level data to estimate whether the wages of temporary immigrants increase after they receive permanent residency. Working with the data from the 2003 NIS, she used immigrants’ initial wages when they first arrived in the United States and their current wages (after receiving permanent residency), and applied difference-in-difference matching using native workers as the control group. She found that immigrants experienced a wage gain of 18%–25% between their first job in the United States and their current job after receiving a green card. She attributed the wage gain experienced by immigrants to the acquisition of a green card. Her approach has several potential shortcomings. First, she used natives as the control group. Assimilation literature argues that new immigrants lack host country–specific capital; as they remain in the host country, they accumulate the human capital needed, thereby narrowing the wage gap between natives and immigrants. This means that for any given level of human capital, an initially large difference between natives and immigrants will narrow over time as immigrants accumulate host country–specific human capital. If this trend occurs, then this narrowing will be interpreted as the green card effect. Gass-Kandilov (2007) estimated an ordinary least squares regression with a binary dummy variable equaling 1 if the immigrant is a new arrivee. Based on this regression, she reported that newly arrived immigrants did not have lower wages than comparable natives after she controlled for other covariates. She interpreted this result as a sign that assimilation and the accumulation of host country–specific capital does not impact the wage of this group of highly skilled immigrants. In her regressions, however, she did not allow the new arrivals to differ from the adjustees in any unobservable way. If their unobservable differences are not identical—for example, the treatment group may have more innate intelligence or are more motivated to work—then such a difference may have introduced a bias in her results. Second, the respondents were interviewed immediately, in most cases within six months, after becoming permanent residents. Some adjustees may not have had time to find and relocate to a new job. In other words, the full impact of the treatment may not have been realized by the time the respondents were interviewed. If this is the case, Gass-Kandilov’s (2007) estimates may be downwardly biased. Because we use wage data from the first job after coming to the United States for both our treatment and control groups, our estimates are less likely to face this problem. Finally, Heckman et al. (1996, 1997, 1998a, b) found that one of the most important criteria under which matching estimators perform well is when the treatment and control group data come from the same sources. This allows earnings and other characteristics to be measured in an analogous way. Because Gass-Kandilov (2007) did not conform to this last condition, her results could be further biased. In this article, we solve these problems by estimating a matching model using the data from immigrants only. We exploit the fact that some of the 2003 NIS interviewees were adjustees (i.e., individuals who were already living in the United States) when they applied for green cards and the others were new arrivees (i.e., they arrived with a green card). Because the newly arrived immigrants came to the United States with a green card, they did not face the frictions that may reduce the wages of temporary immigrants. In other words, the newly arrived immigrants received the treatment—which in this case is the permanent residency. On the other hand, the adjustees, when they first arrived in the United States, did not have green cards and therefore became susceptible to the aforementioned labor market frictions during their first job in the United States. We use the adjustees as our control group. For both groups, we use the wages of immigrants immediately after they migrated to the United States, which means they have very minimal U.S.-specific experiences, thus making the matching more effective (Heckman et al. 1996, 1998a, b; Smith and Todd 2005). Nevertheless, our discussion on unobserved heterogeneity above suggests that matching on observable characteristics may not be enough in this case because there might be time-invariant unobservable differences. Heckman et al. (1997, 1998a, b) and Smith and Todd (2005) concluded that usually difference-in-difference matching estimators produce results that are closest to experimental outcomes because time-invariant characteristics, such as ability, between the treatment and control groups are differenced out. Because we suspect that this may be true in this application, we implement difference-in-difference matching estimation. In the NIS, interviewees were asked about the wages they earned at their last job in their source country before they migrated to the United States. We use the purchasing power parity–adjusted (PPP-adjusted) source-country wages for both the treatment and the control groups as the before-treatment wages in order to implement a difference-in-difference matching estimator. Note that “before income” refers to their income right before they migrated to the United States, and “after income” refers to their income right after they migrated. Because immigrants came to the United States at different points of time, especially those in our control group, the before-after reference used here may not always correspond to calendar time. For example, adjustees (in our control group) who arrived in the United States in 1996 may have both a “before income” and an “after income” during their immigration year of 1996; new arrivees (in our treatment group) who arrived in the United States in 2003 have a “before income” and an “after income” from their immigration year of 2003. To make them comparable, we report all wages at 2003 prices. For the source-country wage, we use the PPP-adjusted data from the NIS. The NIS conducts a PPP adjustment of the wages of immigrants from their host country into U.S. dollars based on purchasing power estimates derived from the Penn International Comparisons Project (Jasso et al. 2000; Jasso and Rosenzweig 1988). The estimates were developed by using a comparison of the costs of living and exchange rate fluctuations between the immigrant’s source country and the United States, allowing an exact comparison of the earnings of different immigrant workers from a variety of host countries (Jasso et al. 2000; Jasso and Rosenzweig 1988). For further details regarding this approach, see Summers and Heston (1991). Before we proceed further, it is worthwhile to discuss some of the potential problems with our current approach. We noted previously that a share of H-1B workers do not ultimately apply for or receive a green card, but in our sampling framework we observe only the H-1B workers who successfully applied for a green card. Nonetheless, if the group that ends up with a green card is either positively or negatively selected, then our estimates would be biased. This bias, however, may not be very important in the current context because the literature suggests that selection may not be a significant problem.5 For example, Chiswick (1980) and Reagan and Olsen (2000) found no selectivity among return migrants. Some authors have reported evidence of selection among emigrants, but these reports are not in agreement regarding whether the selection is positive or negative. For example, Jasso and Rosenzweig (1988) reported evidence of positive selection among return migrants, but Borjas (1987) and Massey (1987) reported evidence of negative selection among return migrants. Finally, Constant and Massey (2003:651) reported that “(I)n congruence with previous studies, we find that cross-sectional earnings results are not substantively distorted by selection biases due to emigration.” In light of the above evidence from these studies, we do not believe that using adjustees as control group is a significant problem in the present context. Also, if discrimination against immigrants exists and that discrimination is changing over time, then we might create a bias in our estimates. For example, if discrimination against immigrants is decreasing over time, then we may overestimate the effect of a green card. Because of the relatively short time frame of our analysis, this is unlikely to be a problem. In addition, if wages in the United States are growing at a faster rate than those in the immigrants’ source countries, then we will also overestimate the green card effect. However, because wages in most of the source countries grew faster than those in the United States during the 1990s we might, if anything, underestimate the effect of a green card. Data Data used in this study come from the New Immigrant Survey (NIS), which provides extensive information on a nationally representative sample of new lawful immigrants. We use the sample of adults (i.e., individuals who were over the age of 18 at the time of the interview) who were the principal applicants and who became permanent residents between May and November of 2003. A total of 8,573 adult immigrants were interviewed between June 2003 and June 2004 after they achieved permanent residency. Our baseline sample consists of 333 individuals for whom we have data on all variables. This sample size is considerably smaller than the original sample size because only 15% (1,389) of all principal applicants are employer-sponsored. Among those employer-sponsored individuals, the source-country wage is available only for 434 individuals. Of those 434 individuals, we drop an additional 101 from the sample because some of the other variables are missing observations, leaving us with 333 individuals. The first four columns of Table 2 present the summary statistics for the variables used for the treatment group (those who arrive with a green card) and the control group (adjustees).6 Most of the control group (about 75%) first entered the United States on a temporary worker visa. The control group (adjustees) arrived earlier, between 1987 and 2003, with about 85% arriving between 1995 and 2000. The immigrants in the treatment group arrived in the United States during 2002 and 2003. The treatment and control groups are not too dissimilar given that this is a non-experimental sample. The variable age refers to the current age for the treatment group; for the control group, age refers to age at the time of the first U.S. job7 because we use their wage in their first U.S. job as our control. The average age of the control group is a little higher (at about 39 years) than that of the treatment group (about 36 years). We use education obtained in the source country for matching between the treatment and the control groups. In the NIS, respondents were asked to report their years of U.S. education as well as their total number of years of education, foreign and domestic, at the time of the interview. We calculate source-country education as the difference between these two variables. The average educational level is about 15.4 years for the treatment group and about 16.5 years for the control group. In the NIS, respondents were asked about their entry into the labor force in their source country and about their last job right before they left their source country. We used this information to construct their source-country work experience. For some of the immigrants who had more than one job in their source country, exact source-country work experience cannot be determined because there is a gap between the time they left their first source-country job and started their last source-country job. Questions about the intervening jobs were not asked in the survey. In these cases, we used potential work experience, which is the difference between the first year and the last year in which they worked in their source country. In our sample, the average work experience for the treatment group is 12.9 years, and the average for the control group is about 11.7 years. We also use their source-country occupations (which are reported using census four-digit categories) for matching. Following Hersch (2008), we group the occupations into five categories: professional and managerial (codes 10–2960), health (codes 3000–3650), service (codes 3700–4650), sales and administrative (codes 4700–5930), and production (codes 6000–9750). Although the data contain information on the occupation of immigrants in the United States, we do not use that information in propensity score matching: having a green card (or not having it) expands (or shrinks) the choices of immigrants in terms of their job search, thereby affecting the occupational status by the treatment itself and hence making it incompatible for use with matching (for a detailed discussion, see Todd 2008). We also match the treatment and the control groups on their source region (Asia, Africa, Europe, and Latin America), religion, gender, and a marital status dummy variable. In the NIS, respondents were asked the following question about their relative family income when they were 16 years old: “Now I’d like to ask you some questions about when you were a child. Thinking about the time when you were 16 years old, compared with families in the country where you grew up, would you say your family income during that time was far below average, below average, average, above average, or far above average?” About 21% of those in the treatment group reported that they are from families with incomes that were above average or far above average, compared with 31% of those in the control. We use respondents’ wages at two different points of time. The “before wage” refers to the respondents’ wages from their last source-country job just before migration to the United States; the “after wage” refers to respondents’ first wages after migration to the United States. For individuals who arrived with a green card, the second wage reflects the treatment (i.e., green card) effect and the repricing of their skills in the U.S. labor market. For adjustees, the after wage captures the revaluation of their skills at the U.S. prices. The differential of these wages would allow us to identify the green card effect. We use hourly wages in 2003 prices for all wage observations. Source-country wages are also adjusted for PPP. In the questionnaire, individuals were asked about payment and pay periods. For salaried individuals, hours of work per pay period are available. We calculate hourly wage rate by dividing total payment in any particular pay period by hours worked. Table 3 shows the wages for the treatment and the control groups. For the treatment group, their average before (source-country) wage was$18.13; their average wage increased to $29.67 after they migrated. For the control group, their average before (source-country) wage was$16.38; their average wage increased to $23.44 after they moved to the United States. Therefore, after moving to the United States, the treatment group experienced a wage increase of$11.54 per hour, whereas the control group experienced an increase of $7.06 per hour. Thus, the simple mean difference-in-difference estimate of the acquisition of a green card leads to an increase of$4.48 an hour, or $8,960 per year (based on 2,000 hours worked per year). This estimate does not take into account the differences between the treatment and control groups that exist in nonexperimental data. To account for such differences, we implement matching estimators. We provide an abbreviated and rather informal discussion on matching estimators based on Smith and Todd (2005) in the Methods section for readers who may not be familiar with these estimators. Please see Heckman et al. (1997, 1998a, b) for more detailed discussion about the properties of these estimators. Methods Let R = 1 denote the treatment of receiving a green card, and let R = 0 indicate not receiving a treatment. Also, let Y1 denote the wage of the treated group with a green card, and let Y0 denote what the wage of the treated group would have been without a green card. The cross-sectional estimate of the value of a green card is therefore given by For the treated group, we observe the mean wage after they receive the green card , but the counterfactual is not observable. A matching estimator allows us to construct the unobservable counterfactual using data from the control group. Matching estimators assume that Y0 is independent of receiving the treatment conditional on a set of observable characteristics (Z). Because we are interested only in the treatment effect on the treated (TT), we require a much weaker assumption—namely, conditional mean independence (Smith and Todd 2005): Rosenbaum and Rubin (1983) showed that when outcomes are independent of program participation conditional on Z, they are also independent of participation conditional on propensity score . We also require that ; that is, for each participant there is a nonparticipant analogue. Then TT can be expressed in the following way: Unfortunately, as argued earlier, cross-sectional matching estimators perform poorly if there are permanent unobserved differences between groups, so a difference-in-difference matching strategy is more appropriate in the current context. This type of estimator is analogous to a difference-in-difference regression, but it does not impose all of the restrictions. We implement a panel data version of difference-in-difference matching estimator: This estimator uses both pre- and post-treatment (t′ and t, respectively) data. The first term is the difference between the U.S. wage (after receiving the green card) and the source-country wage for the treated group. The second term is what the difference would have been between the U.S. wage (without a green card) and the source-country wage for the treatment group. As with the cross-sectional estimate, here the second term (i.e., the counterfactual) is not observable. Again, matching allows us to construct the unobservable counterfactual using data from the control group. In practice, the following estimator (suggested by Todd and Smith (2005)) was implemented: where i denotes the individual and W(i, j) are the weights that depend on the distance between the propensity scores Pi, denotes the set of participants, and I0 denotes the set of nonparticipants. Sp is the region of common support, and n1 is the number of persons in the set . We implement two types of matching: nearest-neighbor and kernel matching. In our empirical implementation, we first use a single nearest-neighbor implementation, followed by a 5- and 10-nearest-neighbor implementation. We also implement a kernel matching estimation procedure. In this case, a match for each participant is constructed using a kernel weighted average over multiple persons in the comparison group. We use normal distribution as the kernel in our empirical implementation. Results Column 1 of Table 4 presents the parameter estimates for the propensity score equation. We use a probit model to estimate the coefficients. The estimates suggest that women and immigrants with more source-country experience are more likely to receive the treatment. We use indicators for bachelor’s degree (more than 16 years but less than 18 years of education) and master’s degree or higher (more than 18 years of education) in our baseline specification.8 Somewhat surprisingly, there is a negative (and statistically significant) correlation between obtaining a graduate degree in a source country and the probability of receiving the treatment. This result is due to the fact that we are also controlling for source-country wage as well as source-country occupation, both of which are correlated with education. In fact, if we do not control for source-country wage (as we do later for cross-sectional matching), the correlation becomes insignificant (in both a statistical and an economic sense). As expected, a higher source-country wage increases the probability of receiving the treatment. Being in a health care–related occupation increases the chance of getting the treatment. This probably reflects the shortage of workers in the U.S. health care field. All the variables in our propensity score specification pass the balancing test. The –pscore– command written by Becker and Ichino (2002) was used to check the balancing criterion. It performs a t test to check that means of covariates do not differ between the treatment and the control groups within propensity score blocks. Block boundaries are determined to ensure that means of propensity score is identical for treatment and control group within each block. See Becker and Ichino (2002) for further details. Our results are not sensitive to reasonable changes in the propensity score estimation specification. We checked other reasonable specifications, including controlling for years of education in addition to degree dummy variables, as well as adding higher-order terms for experience. These do not have any substantive effect on our results. Table 5 presents results from the difference-in-difference estimates using nearest-neighbor matching and kernel matching (using the –psmatch2– command written by Leuven and Sianesi (2003)). Details of difference-in-difference matching are shown in Tables 7 and 8 in the appendix. The first column of Table 5 reproduces the mean difference-in-difference estimate from Table 3. Then we present estimate from nearest-neighbor matching using 1, 5, and 10 nearest neighbors. In all matching estimators, we impose the common support condition. Bootstrap standard errors based on 200 replications are in parentheses. Nearest-neighbor matching estimates show that employer-sponsored immigrants experience a significant wage gain. This wage increase is$5.90 per hour using single nearest-neighbor matching. We also implemented matching based on 5 and 10 nearest neighbors. As we increase the number of neighbors used, the variance decreases but the average of quality of matches also decreases. This is the well-known trade-off between bias and variance of nearest-neighbor matching estimates. Our estimate based on 5 nearest neighbors suggests a wage gain of $6.42 per hour, but our estimate based on 10 nearest neighbors indicates a wage gain increase to$9.67 per hour. Given our relatively modest sample size, using a large number of neighbors may quickly lead to bad matches and therefore to an increased bias. The nearest-neighbor matching estimates are not statistically significant, perhaps because of our relatively small sample size. However, it is important to note that bootstrapping may not produce correct standard errors in nearest-neighbor matching (Abadie and Imbens 2008). Furthermore, the literature suggests that kernel matching may perform better than one-to-one matching.

We next implement kernel matching and use a normal kernel. For the bandwidth parameter, we use Silverman’s (1986) rule of thumb method as suggested by Smith and Todd (2005). The Silverman rule suggests that , where σ is the standard deviation of the outcome variable (i.e., hourly wages) and n is the number of observations. Silverman’s rule suggests a bandwidth of around 6.87. In kernel matching, there is also a trade-off between the bias and the variance: the lower the bandwidth, the lower the bias but the higher the variance. We show robustness to change in the bandwidth parameter. Along with our baseline estimate, we also present estimates for a bandwidth of 1.0 and a bandwidth of 15.0.

We report bootstrap standard errors. Using 6.87 as the bandwidth parameter, matching estimates show that the hourly wage gain from receiving a green card is about $5.93. If we use 1.0 as our bandwidth, the estimate changes to$6.23 per hour; the estimate decreases to $5.93 per hour when we use 15.0 as the bandwidth parameter. All estimates are statistically significant and are not sensitive to changes in the bandwidth parameter in any substantive way. For reasons discussed earlier, we prefer our kernel matching estimates (although they are very close to one-to-one matching estimates in the present context). If we assume that an immigrant is working full-time (2,000 hours per year), then an hourly wage gain of$5.93 implies a wage increase of $11,860 per year. Next, we report the estimates from cross-sectional matching for comparison purposes. As discussed earlier, cross-sectional matching may suffer from unobserved heterogeneity, but it may be informative to compare to the estimates from cross-sectional matching with the difference-in-difference matching reported previously. Another reason for this exercise is that we lost much our sample (about 60%) because we do not have their source-country wages, which are necessary to implement difference-in-difference matching. Smith and Todd (2005) showed that matching estimates can be sensitive to sample choice. For example, they showed that some of Dehejia and Wabha’s (2002) results were driven by their ad hoc sample selection criteria. Although we do not impose any ad hoc restrictions, it still is informative to check the robustness of the estimates to different samples. In cross-sectional matching, we do not need the information on source-country wages and hence our sample is bigger, at 863 observations.9 To that end, we reestimate the propensity scores using a slightly different specification (specification B) than the one discussed previously. In the new specification, we drop the following regressors: log of source-country wage (to increase our sample size) and the indicator for whether the family of the respondent had a higher than average income (because this variable violates the balancing condition in this larger sample). The parameter estimates from the probit model for propensity score estimation are shown in column 2 of Table 4. Table 6 compares the kernel matching estimates based on two samples. Panel A shows the estimates for our baseline sample (333 observations), and panel B shows the estimates for the expanded sample (863 observations). Cross-sectional estimates can be obtained for both samples, but the difference-in-difference matching estimates can be obtained only for the baseline sample. Matching estimates are obtained for specification 1 (column 1 of Table 4) and for specification 2 (column 2 of Table 4). For comparison, cell 1 (row 1, column 1) presents the difference-in-difference estimate of the hourly wage gain based on specification 1 ($5.93). Cell 2 (row 2, column 1) shows the cross-sectional estimate of hourly wage gain associated with an employment-based green card ($7.68). Cell 3 (row 1, column 2) presents the difference-in-difference estimate of hourly wage gain based on specification 2 ($5.37). Cell 4 (row 2, column 2) shows the cross-sectional estimate of hourly wage gain based on specification 2 ($6.97). Since we are keeping the propensity score specification and the sample exactly the same with this exercise (row 1 vs. row 2), we can compare the estimates from the cross-sectional matching to difference-in-difference matching. In both cases, difference-in-difference estimates are smaller than cross-sectional estimates (although they are not statistically different from each other), suggesting that treatment group, perhaps not surprisingly, is “more able” (e.g., individuals in the treatment group may have more innate intelligence or may be more motivated to work) than the control group in unobservable ways. Comparing column 1 to column 2 shows the sensitivity of our estimates to changes in propensity score specification. Again, our estimates are not very sensitive to such changes. Panel B shows the cross-sectional estimate of hourly wage gain associated with an employment-based green card using specification 2 for the larger sample (863 observations). Specification 1 cannot be used for this larger sample because it controls for source-country wages. Estimates show that the acquisition of a green card leads to an hourly wage gain of$8.32. The corresponding estimate is about $6.97 for the smaller sample (333 observations). Both of these two estimates are statistically significant, but the larger sample size leads to a substantial reduction in the standard error. Furthermore, we cannot reject the hypothesis that the estimated effects are the same in the two samples. This result gives us confidence that our relatively small sample size may not be an issue. Finally, to assess whether the conditional independence assumption is satisfied in our sample (given our controls), we perform a specification test (sometimes also referred to as falsification test) as implemented by Smith and Todd (2005). In the present context, this implies that we estimate the green card effect on the source-country wages of the immigrants. If conditional independence is satisfied, our estimated effect should be close to zero. Note that we can implement only a cross-sectional matching (as in Smith and Todd 2005) because we observe the pre-treatment wage only once. Estimates (not presented in tables) show that the green card effect on the pre-treatment (i.e., source-country) wage is an increase of$1.75 per hour (with a standard error of 2.93). Therefore, the estimated effect is not statistically different from zero as expected. The positive point estimate is most likely due to the unobserved heterogeneity (i.e., the treatment group is more able than the control group in unobservable ways). This evidence suggests that matching is valid in the present context and will produce unbiased estimates.

The various estimates using different types of matching as well as using different specifications within a particular type of matching are all close to one another. Additionally, the robustness checks increase our confidence in our estimates. Finally, our preferred estimate, using difference-in-difference kernel matching, gives us an hourly wage gain of $5.93. This translates into a wage gain of 25.4%, which is very close to Gass-Kandilov’s (2007) estimate of a 24.7% wage gain following the receipt of a green card. Conclusion In this article, using data from the New Immigrant Survey, we implement matching estimators to estimate the wage gain experienced by immigrants after they become permanent residents. Estimates show that permanent residency leads to a wage gain of$11,860 per year. This result confirms the popular belief held by both proponents and opponents of highly skilled temporary worker programs that H-1B workers are paid less than native workers. In addition, this article quantifies the size of the gain.

This result shows that the current process of acquiring a green card gives too much power to employers and hinders job mobility among highly skilled immigrants. One way to resolve this would be to increase the quota of green cards awarded to highly skilled immigrants. The current waiting period of 6 to 10 years results in restricted mobility for a long period; increasing the quota would ensure greater mobility, thereby applying upward pressure to the wages of H-1B workers. Note that an increase in the number of H-1B visas approved (like the increase sanctioned by Congress in 2000) may not increase the mobility of temporary workers because even though the H-1B visa can be transferred from one employer to another (as long as the new employer files a petition for the immigrant), the green card application cannot be transferred. Therefore, increasing the cap of the H-1B quota does not really increase the mobility of H-1B workers who have applied for a green card. Indeed, increasing the quota may be counterproductive. If employers pay temporary workers less and the supplies of such workers are increased, it might create additional downward pressure on the wages of comparable natives. On the other hand, increasing the number of permanent residents would mean that employers have to pay immigrants wages similar to those of natives. It would also remove incentives for employers to hire H-1B workers if suitable native workers are available for the job.

Acknowledgments

We would like to thank two anonymous referees and the editor for many helpful comments. The usual disclaimer applies.

Notes

1

We use the terms “green card,” “legal permanent residency (LPR),” and “permanent residency” interchangeably in this article.

2

Extensions on pending green card applications can alter the six-year time interval.

3

In our analysis, we do not distinguish between H-1B and L-1 temporary workers. Although the use of L-1 visa has increased since the late 1990s, the number of L-1 visas issued is still small compared with the number of H-1B visas even though the number of L-1 visas is not capped (Kirkegaard 2005). Given the time frame of our sample, we do not expect the share of L-1 immigrants to be particularly large in our sample. We discuss this issue further in the Data section.

4

Green cards may have a high nonmonetary value (e.g., utility from having relatives close-by, or peace of mind from persecution), but we do not address those issues here.

5

Another level of selection relates to the question of who immigrates in the first place. That selection, although important for other purposes, may not be very important here because our universe consists of only immigrants and not the whole population of the source countries.

6

We also implemented a cross-sectional matching on a larger sample of 863 immigrants. The summary statistics for this group are in the last four columns of Table 2.

7

Alternatively, we could have matched of the year of birth, which would not require this adjustment. But interpretations of coefficients of higher-order terms (like age squared) are problematic. Using year of birth yields the same results.

8

We did not use years of education in our baseline specification because that variable did not satisfy the balancing criterion in the cross-sectional matching sample (discussed later in this section). However, years of education does satisfy the balancing criterion in this sample, and including it in the propensity score specification does not change our estimates.

9

The summary statistics for this sample are presented in the last four columns of Table 2.

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