U.S. Border Enforcement and the Net Flow of Mexican Illegal Migration

U.S. Border Enforcement and the Net Flow of Mexican Illegal Migration Manuela Angelucci First version: October 2003 Current version: June 19, 2010 Abstract I investigate the effect of U.S. border enforcement on the net flow of Mexican undocumented migration, both of which have been considerably increasing in the last three decades. This effect is theoretically ambiguous, as increases in border controls deter prospective migrants from crossing the border illegally but lengthen the duration of current illegal migrations. The inflow and outflow of illegal Mexican migration respond to changes in border enforcement. The effect of enforcement on the inflow has marginal returns that increase with enforcement and is consistent with the hypothesis that tighter enforcement selects more productive migrants. This positive selection makes the outflow sensitivity to marginal enforcement changes comparatively more stable over time. A marginal increase in border controls increases the stock of undocumented migrants between 1972 and 1986, has either no effect or a small and negative effect between 1987 and 1996, and has a larger and significant negative effect between 1997 and 2003. JEL Classification: F22, J61, K42, O15 Keywords: Illegal migration; Border enforcement; Mexico I am grateful to Dan Ackerberg, Orazio Attanasio, Marco Cozzi, Christian Dustmann, Kei Hirano, Jonah Gelbach, Costas Meghir, Cristina Santos, and Adam Szeidl for their constructive and helpful comments. I am indebted to Gordon Hanson for providing border enforcement and apprehension data and to Carmen Carrion-Flores and Todd Sorensen for sharing their data on the appropriations committee composition. All errors are mine. 1

1 Introduction Border enforcement is a cornerstone of U.S. immigration policy. However, while its intensity has nearly tripled between the early 1970s and the mid 1990s, the size of the illegal Mexican migrant population in the U.S. has skyrocketed. This population has grown from 1.1 million in 1980 to 2 million in 1990 and 4.8 million in 2000 (INS Statistical Yearbooks) and it accounts for about 70 percent of the total unauthorized resident population of the United States. The incentives to emigrate out of Mexico have increased in the last few decades, as severe financial crises and demographic pressures in some Mexican states widened the U.S.-Mexico wage gap. Thus, it is possible that illegal migration from Mexico to the United States would have been even higher if enforcement had been looser. Nevertheless, border controls may have perverse effects on the net flow of illegal migration because they influence the behavior of both prospective and current migrants. Higher enforcement may deter prospective migrants from crossing the border illegally. However, while fewer migrants enter the United States illegally, those who do may stay longer, to recoup the higher entry cost. Moreover, higher enforcement may lengthen the stay of seasonal and repeat migrants already living in the U.S.A., as the costs of future migrations will be higher. This second effect is potentially important, given the large size and the historical high mobility of undocumented Mexican migrants. If tougher border enforcement lengthens migration duration, patrolling the border might, to some extent, indirectly encourage the formation of a more permanent undocumented resident community. A similar model describes the effect of enforcement on the productivity of temporary migrants. Higher enforcement selects better migrants by increasing migration costs. However, if individuals are target earners the best migrants in a cohort are also the ones who return home first. The net effect of enforcement on migrant productivity is ambiguous. Understanding which effects prevail is therefore an empirical question. This paper examines how U.S. border enforcement affects Mexican illegal immigration. It makes two contributions to the existing literature. First, it provides estimates of the effect of border enforcement on the net flow of undocumented Mexican migrants between 1972 and 2003 by merging aggregate border enforcement with individual-level data on undocumented migration from the Mexican Migration Project (MMP107). In this way one can observe how border controls affect the likelihood of both undertaking and returning from an illegal migration. Second, it introduces the use of choice-based sampling methods for the Mexican Migration Project data. While being a unique source of information on the characteristics of illegal migrants, with data spanning several decades, high-migration states are over-sampled. Accounting for the choice-based nature of the sampling method considerably changes the estimates of the effect of enforcement on illegal migration. The empirical analysis deals with several econometric issues besides choice-based sampling. First, border enforcement is likely endogenous, as controls may increase in response to expected high migration. I address this issue by using the Drug Enforcement Administration (DEA) budget and 2

the share and seniority of appropriations committee members from border states and districts as instrumental variables. Second, the sample of current migrants is self-selected in a way that is correlated with enforcement (e.g. observable and unobservable characteristics of migrants likely differ in years of tight and loose enforcement). I deal with this self-selection by adding cohort effects. Third, it is possible that different individuals may not be equally sensitive to enforcement changes along different border states. For example, a community with a long history of border crossing through California may be largely insensitive to an enforcement build-up in Texas. To tackle this issue, I alternatively model individuals migration and return decisions as being 1) equally affected by enforcement changes along any border state and 2) affected only by changes in their community modal crossing state. One can interpret the parameters estimated under these different assumptions as bounds to the true effects. There is a growing literature trying to understand the relationship between illegal migration inflow and border enforcement. Some papers use aggregate data on arrests of illegal border crossers (see, e.g., Hanson and Spilimbergo, 1999, Borjas et al., 1991, Espenshade, 1994, and Davila et al., 2001). A number of more recent paper use MMP data to study different features of the relation between enforcement and inflow, e.g. inflow quality (Orrenius and Zavodny, 2005), the illegal crossing market (Gathmann, 2008), and patterns of crossing places (Carrion-Flores and Sorensen, 2006). While most of these latter papers account for enforcement endogeneity and sample selection, none of them accounts for the choice-based nature of the data. Fewer papers study the effect of border enforcement on the outflow. Kossoudji (1992) uses a sample of repeated illegal Mexican migrants to estimate the effect of a past apprehension on current migration frequency and duration, and finds that past apprehensions change the frequency and duration of migrations. Unfortunately, her data has three shortcomings. First, it is a small, selected sample, so it is difficult to generalize her results. Second, it does not permit one to distinguish interior from border apprehensions. Third, it is a sample of migrants only, so one cannot estimate the effect of enforcement on the net flow of migrants. Reyes (2004) uses MMP data to estimate the determinants of changes in trip durations for Mexican legal and illegal migrants. However, she does not address the issues of non-random sample selection, choice-based sampling, and endogeneity of enforcement. This paper has five main findings. First, border enforcement has a significant deterrent effect, i.e. it reduces illegal migration inflow, discouraging prospective migrants from attempting an illegal trip to the United States. At the same time, it prevents some illegal migrants from leaving the U.S. to return to Mexico, partly because they know it would be difficult to migrate back, but also because the higher migration cost increases the trip duration. Second, the marginal effect of enforcement varies by Mexican state and over time. Migrants from traditional sending states are more sensitive to enforcement than migrants from new emigration states. This is likely because the former group of migrants has tended to undertake short, multiple U.S. trips over their life cycle (e.g. Donato et al. 1992). An increase in migration costs caused by higher enforcement may considerably affect the incentives to migrate temporarily, either forcing 3

people to switch to fewer, longer trips (e.g. Hill, 1987 and Kossoudji, 1992), or preventing them from migrating altogether. Conversely, the latter group, with hardly any tradition of illegal U.S. migration, is less sensitive to enforcement. As already mentioned, individuals from these states started to migrate fairly recently, when the level of border enforcement was high, probably in response to labor demand and supply shocks, and are more likely to undertake longer if not permanent migrations. 1 Long-term migrants are hardly affected by changes in enforcement, as the increase in costs is unlikely to offset the high financial benefits from a long-lasting migration. Third, the marginal returns to enforcement are a positive function of enforcement. That is, as the level of border controls increases, its marginal deterrent effect becomes higher, consistent with the idea that there is a threshold level of patrolling agents beyond which further increases in enforcement increase the probability of apprehension. Tighter enforcement increases migration costs, as it is positively correlated with both the share of migrants that hires a smuggler to cross the border and smuggler prices. As these costs become higher, fewer individuals migrate. Fourth, the evidence is consistent with the hypothesis that higher enforcement selects more productive migrants, (e.g. the education gap between illegal migrants and non-migrants decrease when enforcement is higher). As migration costs increase, the average migrant productivity goes up. Thus, while the higher costs mean it takes the same temporary migrant longer to save the desired amount of money and be able to return home when enforcement is higher, only individuals who are faster at reaching the savings target migrate. Because of this selection effect, the outflow s sensitivity to marginal enforcement changes is roughly stable over time. Lastly, while these results suggest that enforcement has become relatively more effective over time, it is important to assess its absolute effectiveness. To do that, I provide back-of-the-envelope estimates of the marginal effect of enforcement between 1972 and 2003. Even under very conservative assumptions, the net effect of enforcement on the stock of migrants is at best zero, and likely positive, between 1972 and 1986. However, the increase in border enforcement makes it gradually more effective over time. While between 1987 and 1996 its net marginal effect on the stock of illegal migrants ranges between zero and a drop by 900, between 1997 and 2003 this effect increases to a drop in 7600 to 8200 illegal immigrants. These results suggest that the currently high levels of enforcement have reduced the stock of Mexican illegal migrants in the United States and increased its productivity. Besides their policy implications, these findings contribute to the debate about the self-selection of Mexican migrants in the United States. While Borjas model (1987) predicts a negative selfselection, Chiquiar and Hanson (2005) find an intermediate selection of Mexican migrants. That is, if migrants were paid according to Mexican wages, they would be concentrated in the middle of the earnings distribution. Chiquiar and Hanson show the observed intermediate selection may occur if migration costs are roughly equivalent for all prospective migrants and wages are positively correlated with skills. My findings are consistent with this conjecture: when border enforcement goes 1 See Hanson and McIntosh (2007) for further details on the changes in relative labor demand that caused this new wave of emigration. 4

up, increasing migration costs, it selects better educated migrants. Since enforcement has increased over time, it may have contributed to improving the skills of illegal immigrants in the United States. 2 The data Table 1 describes the data used, providing their means and standard deviations for the period of interest. The data used come from several different sources: Border Patrol linewatch hours and aggregate apprehension data are from unpublished records of the Immigration and Naturalization Service (INS), the Department of Justice agency that managed border enforcement until 2001. 2 U.S. wage and unemployment data are from the Bureau of Labor Statistics. The Mexican macroeconomic variables used are from the Bank of Mexico. Hanson and Spilimbergo (1999b) describe both the enforcement and the macroeconomic data in great detail. Individual migration information comes from the Mexican Migration Project database (MMP107), containing data from 107 communities in 19 different Mexican states between 1987 and 2004. 3 Every year a number of different Mexican communities (normally 5) are selected in such a way as to represent a range of diverse characteristics (size, ethnic composition, location and economy). Interviewers collect data on a random sample of 200 households from each locality between December and January, months in which migrants tend to return home. Though interviewed only once, all sampled individuals provide information on their lifetime migration experience. For instance, I observe 30 years of information regarding the timing, duration, location, and legal status of migrations of an individual aged 30 when interviewed at time t. If the household head is absent, the interviewer collects the relevant information on his/her current and past migrations from other household members. Interviewees include individuals with past spells of migration (both legal and illegal ones) as well as others who never migrated. Massey (1987) provides further details about the study design. I use these retrospective migration data to build a panel. I study migration decisions starting from 1972 because I observe my main instrumental variable, DEA budget, only since that year (when the agency was created); this also limits the amount of recall error. For example, the sample contains the 1972-1987 migration history of individuals interviewed in 1987 and the 1972-1990 migration history of 1990 interviewees. I include only individuals aged 16 to 55 who cannot migrate legally. That is, a person s migration history is not part of the sample after she acquires legal status, but it is for the years preceding the legalization. In such a way I obtain an unbalanced person-year panel with different entry and exit years. 4 My upper cutoff year is 1996. This is because from 1998 onwards, the MMP sampled localities from different new Mexican states with hardly any migration. This concentration of data from low migration areas at the end of the time period would create an artificial drop in migration rates in the late 1990 s, and a spurious negative correlation with the high enforcement level of those years. 2 The Department of Homeland Security has replaced the INS since. 3 I also include data on a small sample of pilot interviews from 1982. 4 For example, suppose I observe a household head aged 67 in the interview year, 1997. His migration history is in the sample only between 1972 and 1985 (because he turns 56 in 1986). 5

Figure 1 exhibits my key explanatory variable, annual border enforcement level, measured in thousand linewatch hours per border mile. By linewatch hour I mean one hour of patrolling duty along the southwestern U.S. border. This Figure shows that border controls increased more than threefold in the analyzed time period, with particularly steep increases in the late 1970 s, in the mid 1980 s, and from 1992 onwards. The higher intensity of border controls in the mid 1980 s and 1990 s is associated with changes in immigration laws: the first policy change is the 1986 Immigration Reform and Control Act (IRCA), which granted amnesty to a large group of current illegal U.S. residents, introduced sanctions for the employment of undocumented labor, and increased border policing. 5 The second policy change is the 1990 Immigration Act, which introduced caps to legal migration and restricted the family reunification program to immediate relatives. Both these laws are partly a reaction to the increased migration incentives of those years: Mexico was hit by a severe economic and financial crisis in the early 1980 s. With high inflation levels eroding the purchasing power of wages and periodic peso devaluations, more individuals were attempting to work illegally in the United States. 6 The wage differentials decline at the end of the decade, only to increase again in the 1990 s. Figure 2 shows how the relative peso value of Mexican versus U.S. wages changed dramatically during this period. This substantial time variation is useful to identify wage effects on migration. The impact of economic incentives on illegal migration is also noticeable in Figure 3, which shows the sample shares of potential migrants (i.e. all individuals 16 to 55 who are observed in Mexico without a green card) who undertake an illegal migration, and of current illegal migrants who leave the U.S.A. to return to Mexico. The proportion of individuals who migrate nearly doubles between 1972 and 1986, with a peak in 1986-1987, followed by a steep decline. Part of this decrease is likely a consequence of the IRCA amnesty granted to more than two million U.S.-based illegal Mexicans migrants: this results in a large group of individuals simply switching from illegal to legal status, as evident in Figure 4, which reports the share of individuals in the MMP sample who were granted legal status. 7 The improvement of Mexican economic conditions, the toughening of border enforcement, and the introduction of employers sanctions are also additional likely determinants of the trend reversal. Since the number of legal immigrants likely affects the incentives to migrate (or return from a migration) of undocumented individuals, the empirical specifications control for legalizations. The proportion of annual returns from illegal migrations is roughly stable up to the early 1980 s, and increases dramatically when the peso devaluations make the value of U.S. dollar savings much higher in Mexico. As before, the trend is reversed in the late 1980 s coinciding with a reduction in 5 The Border Patrol budget, which has been increasing continuously since 1986, does not reflect the sharp linewatch hours decrease in 1988. Inspection of the monthly linewatch data shows that the lower enforcement in 1988 is concentrated in the month of August. The enforcement intensity of the remaining 11 months is closer to 1987 and 1989 levels. 6 The Mexican real minimum wage decreased by 74% in the first half of the 1980s (Hanson and Spilimbergo, 1999). 7 The total number of Mexican legalizations ranges between 2,200,000 (Bratsberg 1995) and 2,600,000 (INS Statistical Handbook on U.S. Hispanics 1992). 6

economic differentials, a drop in the population of illegal migrants due to the IRCA amnesty, and an increase in border enforcement. 8 I control for changes in economic incentives by computing the peso value of real U.S. hourly manufacturing wages, because illegal migrants are traditionally largely employed in this sector, and on an index of Mexican average production manufacturing hourly wage. I also experimented with hourly construction wages, another sector that attracts illegal labor. The main results are unchanged. 3 Empirical specification and estimation issues I now proceed to estimate the observed magnitude of the effect of enforcement on illegal migration net flow between 1972 and 1996. My empirical approach consists of estimating the effect that changes in border controls have on the individual probability of transition between different states: from staying in Mexico (m = 0) to becoming an illegal migrant (m = 1); and from being an undocumented U.S. resident (r = 0) to returning home (r = 1). Time is discrete and the unit is the year. I model the two transitions separately. I use the MMP data to create the two dependent variables, in which i indicates the i-th individual and t the year. m it takes the value of zero whenever the individual is in Mexico, and of one when the individual migrates to the United States; m it is missing for all subsequent years the person spends abroad. If the individual returns to Mexico and meets the aforementioned requirements, he or she is again included in the sample. r it is zero when an individual lives illegally in the U.S.A., and one in the year the migrant returns home. The variable is missing for all years spent in Mexico between intermediate migrations. Separately estimating the enforcement effect on inflow and outflow is more useful, from a policy perspective, than looking at the effect of border policing on the net flow directly. For instance, suppose the enforcement effect on the net flow of illegal migration is zero. Policy implications could still depend on how much inflow and outflow are sensitive to increases in the enforcement level. In case they both are, enforcement works and one may want to increase enforcement and provide further incentives for illegal migrants to leave the United States. If neither flow is affected by enforcement changes, border policing does not work ; the policy maker would have to look for different policies to stem illegal migration. 3.1 Estimating the likelihood of migrating illegally I specify the likelihood that a potential illegal migrant undertakes a migration at time t as a function of the variables affecting the costs and benefits of migration considered in the theoretical model: P (m it = 1 b t, X it ) = f(α m + β m b t + γ m X it ) (1) 8 An additional reason for the decrease in returns between 1986 and 1988 may be because amnesty applicants might refrain from returning to Mexico while waiting for their legalization application to be processed, a process which may take about two years. 7

where m is a dichotomous variable that takes the value of one when an individual leaves Mexico to undertake an illegal migration, b is border enforcement and X contains variables that influence the migration decision and are potentially correlated with border controls. These are: 1) macroeconomic variables; 2) gender and age of migrants; 3) the number of individuals who obtain legal status. I condition on the U.S. manufacturing real hourly wage rate in pesos and an index of Mexican manufacturing real hourly wage, together with U.S. unemployment, to capture the probability of finding a job once in the United States. The average age and gender composition of potential migrants in my sample changes over time (age increases, while the gender ratio decreases). Since migration is probably a function of these characteristics, failing to control for these variables may create a spurious correlation between the probability of migrating and enforcement. Regarding legalizations, both this variable and enforcement increase at the same time in the second half of the 1980s, as they are two IRCA provisions. Thus, it is important to disentangle these two effects. The higher the legalization number, the lower the volume of both actual and potential illegal migrants. Hence, part of the post-irca decline in both undocumented border crossings and returns from illegal migration is simply the result of a status change, i.e. becoming a legal resident, rather than the direct consequence of tougher enforcement. This effect may be substantial, since more than 2 million Mexicans are estimated to have benefited from the IRCA legalization program. 9 3.2 Estimating the likelihood of returning from an illegal migration For individual i in time period t, the probability of returning from an illegal U.S. trip conditional on being an undocumented U.S. resident is described as follows: P (r it = 1 b t, X it, c ijt ) = f(α r + β r b t + γ r X it + 1996 j=1961 δ r j c ijt ) (2) 9 Migration is likely not a static decision: decisions may depend on both the current environment and on expectations of the future environment. While the econometric specification in (1) is not explicitly dynamic, one can think of its coefficients as the reduced-form coefficient of a dynamic model where migration depends on both current and expected future values of the relevant variables. Hence β m would be the net effect that a marginal increase in current enforcement has on the migration likelihood through both current and expected future migration costs, considering a linear probability model for simplicity: β m P (mit = 1 mit 1 = 0) b t + T s=t+1 P (m it = 1 m it 1 = 0) E (b s) E (b s ) b t One expects the first term P (m it=1 m it 1 =0) b t to be negative, and the following ones, P (m it=1 m it 1 =0) E(b s, positive, with a ) negative net effect. I also estimated a model where current migration decisions are affected by future as well as current levels of enforcement and macroeconomic variables. The estimated coefficients are consistent with the above discussion: higher current enforcement reduces the likelihood of undertaking a contemporaneous migration by decreasing its costs. However, agents anticipate future enforcement to be higher too. This effect increases the likelihood of a current migration by a smaller magnitude than the direct effect on current costs. These results are not presented here, but are available upon request. 8

r it is zero for current illegal migrants who do not return home, and one for those who return to Mexico in time t. 10 The set of X variables is the same as used in the migration likelihood equation, except for the following difference: instead of using aggregate U.S. wage and unemployment data, I replace them with state-specific variables based on the reported state of residence of illegal migrants. 11 One can think about the error term as composed of an individual-specific effect, a time-varying effect, and a white-noise disturbance. This division is helpful to understand the different sources of potential endogeneity. One is the possibility that the enforcement level may be responsive to aggregate shocks to both inflow and outflow, as I discuss in section 3.5. The other one is due to sample selection: since the decision to migrate depends on the intensity of border controls, higher migration costs select migrants with better characteristics (in the sense that their migration is profitable despite the higher costs). Hence, the unobserved characteristics of incoming migrants are likely positively correlated with enforcement in their migration year. This is a cohort effect. Thus, I control for this type of selection by having a set of cohort dummies, c ijt, in equation (2). I define the cohort by the year of arrival in the U.S., j; for example, c i1990t = 1 for all individuals observed in the U.S. at time t who arrived in 1990. 12 In this way I am controlling for the average migrant characteristics in their year of entry. The remaining deviations from means, which are captured by the composite error term, are uncorrelated with the enforcement level. An alternative way to control for the correlation between migrants characteristics and border enforcement is to replace the cohort dummies in equation (2) with the intensity of enforcement in the migration year. I present these results as robustness checks. 3.3 A model with state-specific border enforcement Equations (1) and (2) assume that individuals are equally affected by enforcement changes along any border state. However, prospective and current migrants are likely to have strong preferences as to where to cross the border. For example, the modal crossing state in 57% of the sampled communities is California. This is due to a combination of California being the most sought-after migrant destination and its border being easier to cross than the more arid and less densely populated areas further east. In response to this heterogeneity, the level of border controls varies considerably by state, with each mile along the California border being patrolled about 5 and 7 times more intensively than the Arizona and New Mexico/Texas borders in the sampled years. Previous experience of individual migrants and community migration patterns are important determinants of location preferences for border crossing. For example, a tightening of enforcement 10 Again, the parameter of interest, β r, which measures the marginal effect of enforcement on the likelihood of returning from an illegal U.S. trip, can be interpreted as the sum of the direct and indirect effect of changes in border enforcement on the likelihood of returning to Mexico. Both effects are expected to be negative, as confirmed by a set of estimations not reported here but available upon request. 11 In my sample, 55% of illegal migrants are in California, 15% in Texas, and 8% in Illinois. I use aggregate wage and unemployment data for the remaining migrants (most of whom do not report state of residence). 12 The base category is 1960 and earlier. This variable has a subscript t because the cohort effect refers to the last migration. Therefore, individuals with multiple migrations have a time-varying cohort effect. 9

along the Texas border is probably going to affect individuals or villages specialized in crossing through its border much more than people or villages that primarily cross through California. One simple way to capture this heterogeneity in the effect of state-specific enforcement changes is to assume that prospective migrants are affected only by enforcement in the community modal border-crossing state, while current migrants are affected only by enforcement in their crossing state. 13 This is the case if, for example, there are high costs to acquire information about specific points of entry, which is somehow confirmed both by anecdotal evidence (migrants learn the best times to cross the border in specific points) and by observing that migrants tend to cross the border in the same state during different trips. The corresponding regressions are: P (m ist = 1 b st, X ist, d s ) = f(α m + β m b st + γ m X ist + s θ m s d s ) (3) P (r ist = 1 b st, X ist, c ijt, d s ) = f(α r + β r b st + γ r X ist + s 1996 j=1961 δ r sjc ijt d s + s θ r sd s ) (4) where b st is the enforcement level of border-crossing state s, the variables d s are border state fixed effects, and all the other variables are unchanged. Therefore, the probability that prospective migrant i from a village with a modal crossing state s will migrate at time t is only a function of the level of enforcement at state s. Likewise, the decision of a current migrant to return to Mexico depends only on the enforcement level in his crossing state s. I estimate the annual village modal crossing state. About 10% of the villages had bimodal crossing states. In these cases I compute the modal crossing state by decade. About 55% of all village-year crossings occur in California and 25% in New Mexico. Migrants in most villages always cross through the same state. The assumption that the migration and return decisions are either affected equally by enforcement changes in different crossing states or affected only by enforcement changes in one particular state are probably too extreme, as these decisions are likely influenced by enforcement changes across all crossing states, albeit to different extents. Therefore, one could interpret the estimates of the effects of border controls from the models with aggregate and state-specific enforcement as bounds to the true effects. One advantage of the latter specification is that one can exploit both the longitudinal and the cross-sectional variation in enforcement. 3.4 Choice-based sampling The MMP data are likely not representative samples of the population of current and potential illegal migrants for two different reasons. First, when the individual migration history data are used as a panel, the number of available annual observations does not follow the same trend as the respective populations, as can be seen in Figure 5. This Figure compares the actual Mexican population (from INEGI) and the stock of current illegal Mexican migrants in the U.S. (from the INS Statistical 13 There is not enough independent longitudinal variation in state-specific enforcement to estimate a model where the migration and return likelihoods depend on each state s enforcement level separately. 10

Yearbooks) with the observation for the MMP samples of prospective and current illegal migrants. I standardize these four variables to ease their comparison (that is, for each variable I create its standardized version by subtracting its mean and dividing by its standard deviation). The dashed lines show the populations, and the solid lines the MMP estimates. Consider the populations as proxies of the stock of potential and current migrants. While both populations grow over time, the samples grow until the mid 1980 s and then decline. This is because of the retrospective nature of the data: for example, while data on 1980 migrations and returns are available from all the respondents interviewed between 1980 and 2006, only the 1996 to 2006 respondents can provide data for 1996. Therefore, the two sets of curves differ considerably in the more recent years. Second, the MMP data over-sample high migration states, especially in the earlier years of its implementation. This results in too high a share of potential migrants from traditional, highemigration states. For example, Table 2 shows that about the same proportion of potential migrants - roughly 6.5% - are sampled from the states Zacatecas and Veracruz. The former is a traditional, high-migration state, while the latter is a new, low-emigration state. The true population proportions differ considerably from the sample ones, as they are respectively 2.8 and 12.4%. The over-sampling of high-migration states affects the composition of the current migrant population by much less. This is because a mix of high and low-return states are given high weights in the sample of current migrants. For example, both the low-migration, low-return states of Chihuahua and Veracruz and the high-migration, high-return states of Guerrero and Oaxaca are under-represented. These issues are important if the effect of border enforcement on illegal migrations and returns from illegal trips vary by state and over time, as is likely the case. To address both of them, I re-weight the data following Manski and Lerman (1977). That is, I compute the ratio between the true probability of being sampled (Q) and the observed sampling probability (H): w et = Qet H et. For potential migrants, Q is the ratio between the state (e) and the total population of all sampled states. I compute it using data on Mexican population by state from INEGI, the Mexican National Statistics Institute. For current migrants, I use the number of individuals by state who are in the US in each given year divided by the Mexican illegal migrant population in the US, using the INS Statistical Yearbooks estimates of the stock of illegal migrants. For example, if 10 migrants from state e are illegally in the US in year t and there are overall 100 migrants in the US in the same year, the corresponding Q et is 0.10. These weights account for the fact that both the potential and current undocumented migrant populations are growing over time and ensure that the estimates are representative of the sampled states, as long as the sampled communities are randomly selected within a state, or migrant behavior is fairly homogeneous within a state. This is likely the case, as state of origin has historically been a strong correlate of Mexican migration to the US. The population of the sampled states is roughly 58% of the total Mexican population in the sampled year; this proportion has been stable between the 1970 s and the 1990 s. One way to summarize whether re-weighting the sample will likely affect the estimation of the effect of border enforcement on the inflow and outflow of illegal migration is to compare the un- 11

weighted and weighted shares of the individuals undertaking an illegal trip and returning from one. While there is a 27% difference for the former (the weighted share of people undertaking an illegal trips is 0.021 while the un-weighted share is 0.029), there is only a 5% difference for returns from illegal migrations (the un-weighted and weighted shares are 0.58 and 0.54). This suggests that accounting for the choice-based nature of the sample considerably changes the composition of the potential migrant population, potentially affecting the estimate of the enforcement effect on migration inflow, but it does not change by much the composition of the current illegal migrant population. I will show to what extent re-weighting the data has a sizeable effect on the estimation of the parameters of interest after discussing the main results. 3.5 Addressing the endogeneity of border enforcement Border controls may be endogenous because the enforcement level may be correlated with unobservable shocks to the migration and the return decisions (Hanson and Spilimbergo 1999b). This endogeneity probably causes an upward, or attenuation bias in the coefficient of border enforcement, for two reasons. First, classical measurement error in enforcement biases its coefficient towards zero. Second, unobserved determinants of migration are probably observed and acted upon Border Patrol. For example, consider the case in which political instability and social unrest increase the incentives to leave Mexico. Border Patrol would observe this and respond by increasing enforcement. That is, the unobserved migration determinants would be positively correlated to both enforcement and migration, causing an upward bias. The relationship between unobserved determinants of returns from illegal migrations and border enforcement is more complex. It is unlikely that enforcement is sensitive to expected outflows of illegal migrants who return back to Mexico. The goal of border enforcement is to prevent undocumented entries in, not exits from the U.S.. Consistent with this view is the evidence from Banks (2007), who shows that the public opinion is actually not affected by the stock of illegal immigrants currently residing in the U.S., which is hard to observe. Thus, it is improbable that the pressure to increase enforcement increases when the stock of illegal migrants is higher. However, there are unobserved determinants of returns that are also correlated with enforcement intensity. For example, the aforementioned political and social instability decrease the incentives to return from an illegal migration and increase enforcement (because they increase the migration incentives). This would cause a downward or amplification bias. At the same time, measurement error introduces a bias towards zero. In sum, the different sources of endogeneity bias the estimate of the enforcement coefficient in opposite directions. I ll return to the effects of endogenous enforcement on the estimates of its coefficients after presenting the results. To address this issue I use two sets of instrumental variables. The first variable is the Drug Enforcement Administration (DEA) budget, which I observe since the agency creation in 1972. Drugs are smuggled in massive quantities through the U.S. Southern border, and one of the aims of patrolling the border is to curb narcotics trafficking. The basic idea behind the use of this instrument is the following: border linewatch hours depend on U.S. preferences over migration 12

and drug trafficking. The first source of variation is certainly endogenous, while the second one is potentially exogenous. Changes in U.S. distaste for drugs (e.g. a tougher War on Drugs ) simultaneously increase the DEA budget and border linewatch hours. While there are obvious overlaps in the two agencies objectives, and the occasional collaboration in specific operations, the Border Patrol primarily undertakes linewatch duties, while the DEA focusses more on drug seizures at storage or production facilities, both in the interior and internationally. The instrument is valid if changes in the DEA budget are uncorrelated with unobservable migration determinants. While I cannot formally test this identification assumption, I can test whether there is a correlation between the DEA budget and observable migration determinants, such as wages and unemployment in Mexico and in the U.S.A.. If DEA budget responds to observable migration determinants, it may be more likely to be affected by unobserved determinants as well. I found that these variables are not significantly correlated with the DEA budget. The instrument would also be invalid if the drugs and illegal migration markets were related (for instance, migrants may smuggle drugs to the United States to finance their trip). In that case, an exogenous change in drug prices, for example, may contemporaneously affect both illegal migration and the DEA budget. I am not aware of direct evidence of the separation of the drugs and illegal migration markets. However, indirect and anecdotal evidence regarding the time period covered by the sample abounds. The Economist (2005) reports that, while in the last few years the two markets have begun to overlap, with some migrant smugglers having illegal border crossers carry drugs, this phenomenon is quite recent. The DEA History Book explains that this phenomenon coincides with the mid 1990 s increase in methamphetamine trade by Mexican criminal organizations, and that methamphetamine producers distributed this drug also using or intimidating illegal aliens. In the time period covered by my data, migrant smugglers are primarily former migrants and do not belong to sophisticated organizations. For my second set of instruments I follow Aghion, Boustan, Hoxby, and Vanderbussche (2005) and Carrion-Flores and Sorensen (2006), using information on the composition of the appropriations committee in the previous fiscal year. I consider the share of the House appropriations committee members from border districts or states for aggregate enforcement and the highest seniority level of border state Senators in the appropriations committee for the state-specific enforcement. The appropriations committee approves the budget of all governmental agencies. The appointment to the appropriations committee is extremely advantageous, since its members can influence pork barrel spending, maximizing their chance of re-election. Thus, committee members from border districts have huge incentives to lobby to increase the Border Patrol budget. The political influence of committee members and the scope for promoting self-serving spending is likely a positive function of their seniority. The appointment to the appropriations committee is largely based on a comparison of candidates expertise and seniority. As Aghion et al. (2005) point out, this ensures the committee composition is unlikely correlated with contemporaneous features of a given state, as it rather depends on the interaction of current and past political histories of all states. This rules out potential correlations 13

between state-specific, time-varying anti-immigration sentiments or policies that may affect the likelihood of undertaking or returning from and illegal migration. Further, Border Patrol budget is only a tiny share of the overall federal budget, and the control of more resources is at stake. Therefore migration issues do not seem to be a main determinant of these appointments. The appropriations committee composition would not be a valid instrument if it caused a change in the incentives to migrate in ways other than through changes in border enforcement. The members of the appropriations committee may increase spending on programs - such as construction projects - that may attract illegal migrants. These programs would likely affect labor market outcomes such as wages and unemployment rates. For this purpose, all migration regressions control for wages and unemployment at the national level and all return regressions control for wages and unemployment of the state of residence, as discussed in Sections 3.1 and 3.2. 14 The composition of the appropriations committee does not seem to affect the incentives to migrate illegally, by, for example, changing access to welfare for illegal aliens. For example, in unreported regressions I reject the hypothesis that either seniority or share of appropriations committee members from border districts are negatively correlated with welfare participation of illegal migrants. This provides indirect evidence that the composition of the appropriations committee does not affect other programs related to migration. Figure 6 shows the standardized instruments at the aggregate level and state by state. aggregate instruments are non-stationary, as I can never reject the hypotheses that each of these variables has a unit root. Nevertheless, the variables are cointegrated, thus the significance of the instruments is not due to a spurious correlation. The pattern is more mixed for the state-specific variables. Table 3 shows the first-stage regressions. The The F tests of the instruments joint significance show there is a strong correlation between enforcement and the instruments. 15 The signs of the instrument coefficients are as expected. Increases in DEA budget and in the share of appropriations committee members from border sector or state members are positively correlated with linewatch hours per border mile. The seniority variable reports the ranking of the appropriations committee senator from a border state with the highest seniority (e.g. the most senior senator has a ranking of one). A drop in seniority by one rank is associated with an enforcement decrease. To appreciate the magnitude of these partial effects I computed their elasticities at the mean of the respective variables. These elasticities vary between 0.11 and 0.37 for DEA budget, between 0.29 and 0.40 for committee members from border states, and between -0.03 and -0.06 for seniority. 14 In unreported migration regressions, I also replaced the national wages and unemployment in the migration regressions with the average wages and unemployment of the three states with most illegal Mexican residents (California, Texas, and Illinois). The estimates of the enforcement coefficients do not change. While I use manufacturing, and not construction wages, the two wage series are very highly correlated. 15 I choose the set of variables that do not reject Hansen s overidentification test (whose null hypothesis is that the instruments are valid) and have a sufficiently large F test for the joint significance of the instrument. 14

4 Results 4.1 The effect of border enforcement between 1972 and 1996 I estimate equations (1) and (2) using a linear probability model and clustering the standard errors at the year and residence state/year level, as I explain in the respective Tables. 16 coefficients as local linear marginal effects at the mean of the explanatory variables. I interpret the Table 4 reports the marginal effect of aggregate border enforcement on the likelihood of undertaking an undocumented migration. The first two columns use pooled data and compare OLS and IV estimates. The estimated effects are negative and significant, and the IV estimates are larger (in absolute value) than the OLS ones. This consistent with both measurement error in enforcement and an upward biased caused by a correlation between unobserved migration determinants and enforcement. However, the OLS and IV enforcement coefficients are not statistically different from each other, neither in this table nor in all the remaining ones. This is likely due to the limited longitudinal variation in enforcement. The elasticity of the IV estimate is -0.41, negative but less than one (in absolute value). The third and fourth columns show how these elasticities change if we use the data as a time series, using as dependent variable the fraction of individuals who undertake an illegal migration each year, ˆMt = i m it/n t, where n t is the number of observations in each year. I estimate this time-series both in levels and first-differencing the data. This latter method provides consistent estimates even in the presence of non-stationary, non-cointegrated variables. I did this although the GLS Dickey-Fuller test rejected the non-stationarity of the residual from the main regression. 17 The effect of enforcement from the time-series regressions is still negative and significant. However, while the levels elasticity is similar to the previous set of results, the first-difference specification shows a higher sensitivity of the inflow to border enforcement. Further, the results from this regression are less reliable also because the instruments are weakly correlated with enforcement, therefore the estimate of the effect of enforcement has a large bias. While higher enforcement reduces the inflow of illegal migrants by increasing migration costs, to understand the effectiveness of this policy one needs to estimate its impact on returns from illegal trips. I report these estimates in Table 5. This Table has a similar structure as the previous one: the first two columns show the main results using the pooled data. The remaining three columns are robustness checks. In column 2.1 I replace the cohort effects with the enforcement level and the economic conditions at migration. The idea is that different enforcement intensities and economic conditions select migrants of different productivity levels, so enforcement at migration is a proxy of the cohort productivity. For example, higher enforcement should select higher-productivity migrants. In columns 2.2 and 2.3 I use the data as a time series. These latter regressions use as dependent 16 I also considered standard errors clustered at the individual level. In all cases, these latter standard errors are smaller than the ones reported in the Tables. 17 In these tests, I assumed that the residuals from both the migration and the return regressions are mean stationary under the alternative hypothesis. 15