The labor market effects of Venezuelan migration to Colombia: reconciling conflicting results^†

Between 2015 and 2019, approximately 1.8 million Venezuelans fled into neighboring Colombia, largely fleeing poverty and violence induced by the economic and political crisis in Venezuela. This large and unprecedented migration wave increased Colombia’s population by almost 4% and stimulated debate over the potential positive and negative economic consequences of the migration. The Colombian case is part of an alarming trend of increasing forced displacement around the world: the United Nations High Commissioner for Refugees (UNHCR) estimates that the number of forcibly displaced worldwide increased from 41 million to 79.5 million between 2010 and 2019.

In the canonical framework, an exogenous increase in labor supply induces a wage decrease when labor demand is sloping downward or a decrease in employment when wages fall below the reservation wage. Labor is distinguished by characteristics such as education, experience, or sector, and the effect of migration on any particular subgroup thus depends on the composition of migrants and their degree of substitutability with natives (Peri, 2016; Ottaviano and Peri, 2012; Borjas, 2003; Altonji and Card, 1991). Firms also react to increased labor supply by investing in additional capital, and we therefore expect persistence of economic effects to decrease with the speed of capital adjustment. Moreover, migrants boost consumer demand, transfer human capital and networks (Bahar et al., 2019, 2020), and can stimulate firm technological upgrading and native occupational upgrading (Foged and Peri, 2016). Thus, the effect of migration on native labor outcomes is not always expected to be negative and will vary depending on the characteristics of both the migration wave and the labor market. In general, when there are detrimental effects, we expect to see them most concentrated on natives with similar skills and working similar jobs as migrants.

The context of Venezuelan migration to Colombia is unique and interesting for various reasons. First, this is a developing country setting, in which around 60% of natives and 90% of Venezuelan migrants are in the informal sector, defined according to enrollment in mandatory health and pension schemes. The informal sector has no minimum wage and tends to have high turnover rates, increasing wage flexibility (Agudelo and Sala, 2017; Guriev et al., 2019).

Many Venezuelans in Colombia have access to legal work status. However, in practice, the vast majority remain in the informal sector, where lack of work status is not a barrier to employment.

In the first part of this paper, I study the effects of migration on native Colombians’ economic outcomes. I do this using variation in the migration rate across 79 metropolitan areas constructed according to commuting patterns, data on the labor market outcomes of migrants and natives obtained from the official labor survey of Colombia (the Colombian National Integrated Household Survey (Gran Encuesta Integrada de Hogares [GEIH]), and an instrumental variable (IV) strategy based on historical migration rates. I find that a 1 percentage point (pp) increase in the migrant share of the population decreases native hourly wages by 1.05%, and this decreases to −0.59% after accounting for region-specific time trends. In 2019, the migrant share across metro areas varied from 1% at the 10th percentile to 8.6% at the 90th percentile, over which an effect size of −0.59 is associated with a 4.5% wage decrease. While these wage effects do not vary significantly by age and gender, they are larger for less-educated natives, especially those who are in the informal sector, are self-employed, or are working in low-skill occupations. These magnitudes are larger than those typically observed in the literature and are consistent with evidence that the economic effects of migration tend to be largest in middle-income developing countries, especially for less-educated workers in the informal sector (Verme and Schuettler, 2021).

Unlike with earnings, I find little evidence for effects on the employment margin, consistent with Colombian workers having low reservation wages. There is no effect of migration on unemployment. Among natives younger than 25 years of age, migration causes a reduction in labor force participation, which is partially explained by a reduction in school dropouts; however, this is not robust to the dropping of metro areas close to the Venezuelan border with high migration rates.

This analysis is “nonstructural” in that it makes no assumptions about mechanisms, which may include any of those discussed at the start of this Introduction. This approach is the most common in the literature studying the labor market effects of migration, and it is informative about the total effects of migration overall and for subgroups of natives, for example, by age, gender, education, or sector (Dustmann et al., 2016).

In another paper (Lebow, 2022), I study this same migration wave by estimating a production function with imperfect substitutability between migrants and natives (Ottaviano and Peri, 2012; Manacorda et al., 2012). This entails making explicit assumptions about the structure of production, which allows me to estimate counterfactual wage effects under alternative scenarios, such as one in which migrants do not downgrade. The estimated wage effects loosely match the nonstructural estimates presented in this paper.

After estimating this baseline specification, I conduct a sensitivity analysis for various specification choices, including choice of instrument, unit of geographic variation, migration data source, and definition of the migration share. The motivation for this is that a variety of studies have used a similar approach to study Venezuelan migration in Colombia (Caruso et al., 2021; Delgado-Prieto, 2021; Penaloza-Pacheco, 2021; Santamaria, 2020; Bonilla-Mejía et al., 2020). While they are consistent in finding negative hourly wage effects concentrated on less-educated natives, they find wildly different magnitudes for those wage effects, ranging from −0.5% to −7.6% in response to a 1 pp increase in the migrant share.

Another paper (Rozo and Vargas, 2021) studies the effects of Venezuelan migration on right-wing voting in Colombia. It also looks at economic outcomes and finds imprecise negative wage effects for natives. However, the magnitudes are not directly comparable with those in other papers because the authors estimate the effect of a change in the predicted migrant share, rather than the observed migrant share.

To illustrate this concept, let “M1” represent the share of the population of migrants who arrived in the past 12 months, and let “M5” represent the share who arrived in the past 13–60 months. Regress the average native log-wage in region k and year t on M1_kt with region and year fixed effects

The fixed effects are not necessary for this exercise, but I have included them to match the typical specification in the literature.

Assume M1_kt and ∊_kt are uncorrelated conditional on the fixed effects. Let the true effect of M1_kt and M5_kt on lnW_kt be α₁ and α₅, respectively. Then, β, the marginal effect of M1_kt on lnW_kt (suppressing conditionality on the fixed effects from the notation for brevity), is obtained as follows: (2) β^=∂lnWkt∂M1kt=α1+α5∂M5kt∂M1kt \hat \beta = {{\partial \ln {W_{kt}}} \over {\partial M{1_{kt}}}} = {\alpha _1} + {\alpha _5}{{\partial M{5_{kt}}} \over {\partial M{1_{kt}}}}

Thus, excluding M5_kt from the regression generates an omitted-variable bias equal to α5∂M1kt∂M5kt {\alpha _5}{{\partial M{1_{kt}}} \over {\partial M{5_{kt}}}} . Only if the excluded group is uncorrelated with the included group, or if the excluded group has no effect on native labor market outcomes, will this omission not generate a bias. If an instrument is being used for M1_kt, in which case, M1_kt can be replaced with M1^kt {\widehat {M1}_{kt}} in the above equations, then the problem persists so long as the instrument is also correlated with the excluded group. In this case, the instrument based on historical migration rates is correlated with both 1-year and 5-year migrant shares, as well as with both foreign-born and return migrant shares. In the analysis in this paper, a regression of M5_kt on the predicted M1^kt {\widehat {M1}_{kt}} and year and metro area fixed effects generates a coefficient of 2.6, such that even a small value of α₅ will substantially bias β^ {\hat \beta } . For example, the true values of α₁ and α₅ could be −1.5 and −0.8, respectively (consistent with a model in which the effects of migration dissipate over time), and this would generate a coefficient β^=3.5 [since−1.5−(0.8×2.6)=−3.5] \hat \beta = 3.5\;\left[ {{\rm since} - 1.5 - \left( {0.8 \times 2.6} \right) = - 3.5} \right] , much larger than the true α₁ of −1.5. As I will show, this is the estimate of β^ {\hat \beta } when I only include past-year arrivals in the migrant share. As made clear in Eq. (2), many other plausible effect sizes α₁ and α₅ would also be consistent with this estimate.

Of course, there are many theoretical reasons to believe that the economic effects of migration may differ according to migrant characteristics, such as time of arrival, return-migrant status, or demographic characteristics. For example, the economic effects of migration tend to dissipate as capital mobilizes. In order to study this, one could include both M1_kt and M5_kt together on the right-hand side, and this is a useful approach if there is sufficient independent variation in these variables to precisely estimate these coefficients. However, when an instrument is being used to account for the endogeneity of the migrant share, this approach requires two instruments to generate independent variation in M1_kt and M5_kt. In practice, such instruments are often difficult to find. If the groups are correlated, then in the absence of independent exogenous variation in each group, one must either estimate the average effect of both groups jointly, assume that the excluded group has no effect on labor market outcomes, or accept the bias that results from studying a group in isolation.

Note that it is not satisfactory to simply use an instrument for one group, M1_kt, while controlling for the other, M5_kt. If M5_kt is correlated with the instrument and the error term, this is an “endogenous controls” problem and β_b will be inconsistent. See Frölich (2008) for a discussion of endogenous controls in ordinary least squares (OLS) and two-stage least squares (2SLS) models. Nonparametric methods may allow for consistent estimates in the absence of a second instrument for M5_kt, but this is demanding and requires extensive independent variation in the endogenous variables.

It is worth noting that this discussion is closely related to one in the migration economics literature around the use of the “skill-cell” approach, in which data are divided into education-experience cells and labor outcomes are regressed on the cell-specific migrant share and cell fixed effects. This approach identifies the “partial effect” of migration on wages within an education–experience group given fixed supplies in other groups. It therefore does not account for potential effects on workers across cells, which is a necessary component of the total wage effect (Ottaviano and Peri, 2012; Dustmann et al., 2016).

In the remainder of the paper, I conduct additional analysis that extends on the existing literature. I fail to find evidence for nonlinear effects of migration on the logarithm of wages, though there is not enough variation in the data to identify nonlinear effects at very high migration rates. I document a small internal migration response to the Venezuelan migration, and I confirm that native spatial arbitrage does not bias labor market estimates in this context (Borjas, 2003; Borjas and Katz, 2007; Monras, 2020). I study native employment across occupation skill groups ranked according the premigration mean years of schooling in each occupation. I find little average effect on occupational skill level and small movements among some demographic groups. Men with completed secondary schooling experienced minor upgrading from low- to middle-skill occupations, while men with postsecondary education experienced minor downgrading from high- to middle-skill occupations, alongside increases in self-reported underemployment. There is also a small movement of natives out of the formal sector in response to the migration. Thus, while some studies have found that migration stimulates native upgrading to higher-skill occupations (Peri and Sparber, 2009; Foged and Peri, 2016; Peri et al., 2020), in this context, this did not occur on a large scale, though there were winners and losers among some subgroups. Finally, I document that wage effects are slightly larger in locations with higher baseline informality rates and lower ease of starting a business as measured in the World Bank Doing Business report, indicated that local economic characteristics are relevant for the economic consequences of migration.

Importantly, the results from this paper are short term, and both theory and existing empirical evidence predict that the effect of migration on native wages should recover and possibly become positive in the long term (Edo, 2020; Verme and Schuettler, 2021). However, this is not necessarily true for the distributional consequences of migration, which often persist. The results motivate policies to support lower-income workers during large migration waves, as well as further research to better understand the mechanisms that drive the aggregate and distributional consequences of migration in the developing-country setting, to enable policy-makers to minimize the costs and maximize the benefits of migration.

This paper proceeds as follows. Section 2 reviews the literature, and Section 3 gives the background on Venezuelan migration to Colombia. Sections 4 and 5 review the data and empirical specifications, and Section 6 presents the baseline results. Section 7 tests the sensitivity to various specification choices and uses these results to reconcile findings in the literature. Sections 8 and 9 conduct additional robustness tests and analysis, and Section 10 concludes.

The magnitude of the average wage effect found in this paper is large but not unheard of in the literature, in the context of a large, sudden migrant arrival and short-run outcomes. For example, Edo (2020) finds that the repatriation of Algerians to France led to native wage effects between −1.3% and −2%, though wages recovered after 10 years. Dustmann et al. (2017), studying the 1991 inflow of Czech workers into Germany, find that the corresponding elasticity is a smaller 0.13% fall in native wages alongside reductions in employment. Studies of migration from the former Soviet Union to Israel in the 1990s also find small negative wage effects concentrated among less-educated natives, which disappear after 4–7 years (Cohen-Goldner and Paserman, 2011; Friedberg, 2001). For various other episodes of forced displacement in high-income settings, the literature has found little-to-no effects on native employment or wages. This includes Cuban refugees in Miami in the mid-1980s, refugee dispersal in the United States between 1980 and 2000, migration from former Yugoslavia into the European Union (EU), and Puerto Ricans in Orlando after Hurricane Maria (Peri et al., 2020; Peri and Yasenov, 2019; Clemens and Hunt, 2019; Mayda et al., 2017; Card, 1990), though the lack of null results has been disputed in some cases (Borjas and Monras, 2017; Borjas, 2017). In other settings, effects are positive: Foged and Peri (2016) find that refugee dispersal in Denmark in the late 1980s increased native low-skill wages and increased the complexity of native jobs. In a recent meta-analysis of the forced-displacement literature, Verme and Schuettler (2021) find that native wage and employment effects are typically insignificant, and when significant, they tend to be negative. These negative effects tend to be the largest for less-educated and informal workers, in middle-income countries, and when the migrant supply increase is large relative to the native workforce. These effects tend to dissipate after 5 years.

An emerging literature studies the economic effects of forced displacement in low- and middle-income countries. An important example is the Syrian refugee migration to Turkey, where the increase in supply was also mostly in the informal sector. Studies of this migration wave find negative effects on native informal employment, alongside positive effects on formal employment (Del Carpio and Wagner, 2015; Ceritoglu et al., 2017; Tumen, 2016; Altındağ et al., 2020) and increasing native task complexity (Akgündüz and Torun, 2018). This could result from language and cultural barriers creating the potential for communication-intensive occupational upgrading by natives (Peri and Sparber, 2009). While many studies find negligible wage effects in Turkey, Aksu et al. (2018) find a negative wage effect in the informal sector, which decreases with education, and Cengiz and Tekgüç (2021) find imprecise negative wage effects in the informal sector using a synthetic control method. As discussed, one reason that wage effects may be larger in Colombia is that Venezuelan migrants speak the same language, increasing substitutability with natives. Another is that employment effects are smaller in Colombia, leaving effects concentrated along the earnings margin.

Various papers in Africa have evaluated, in the low-income country setting, the impact of forced displacement on nearby communities. This setting can be characterized by refugees hosted in camps and large inflows of foreign aid, which differs heavily from the Colombian context as I discuss in Section 3. These studies have generally found positive effects on local employment and household consumption (Alix-Garcia and Saah, 2010; Maystadt and Verwimp, 2014; Ruiz and Vargas-Silva, 2015; Alix-Garcia et al., 2018).

Studies of the economic effect of Venezuelan migration in other countries in Latin America have also found evidence for negative native wage effects mostly concentrated on less-educated and informal workers in Ecuador (Olivieri et al., 2021), Brazil (Zago, 2020), and Peru (Morales and Pierola, 2020).

More recent estimates from Peru show less clear evidence of negative wage effects (Boruchowicz et al., 2021). A possible explanation is migrant selection - Venezuelans who go to Peru are even more educated on average than those who go to Colombia.

Between 2015 and 2019, around 4.5 million people fled Venezuela, making Venezuelans the second-largest internationally displaced population after Syrians (UNHCR, 2019). The primary reasons for this migration were to escape poverty and violence induced by the political and economic crisis. Following the sudden collapse of global oil prices in 2014, Venezuela entered an economic recession that led to hyperinflation by 2016. By 2018, the gross domestic product (GDP) had contracted by 45% since 2013, and around 90% of the population was estimated to be living in poverty. More than 20% of the population was undernourished, access to water and electricity became increasingly scarce, and an estimated 85% of essential medicines were scarce. The murder rate also rose to one of the highest in the world (Wilson Center, 2019; Reina et al., 2018; World Bank, 2018). The primary reasons for migration that Venezuelans cite include shortages of food and medicine, violence and insecurity, lack of access to social services, and fear of political persecution (UNHCR, 2018).

Colombia, the neighbor closest to the population centers of Venezuela, received an estimated 1.8 million of these migrants, more than any other country. Figure 1 shows that this is the first time that Colombia has received a large migration wave from another country: in the 1993 census, 0.13% of the population was Venezuelan born and 0.2% was born in a different foreign country, and these rates remained relatively constant until the onset of the Venezuelan migration in 2015.

The lack of migration into Colombia pre-2015 reflects the fact that Venezuela was historically a recipient, rather than a source, of immigrants. Favorable economic conditions and generous social programs attracted migrants from across Latin America, including Colombians fleeing the decades-long civil war in Colombia (Freitez, 2011).

Figure 1

Figure 2 shows the migrant share of the population across 79 metro areas in 2019, where a migrant is defined as someone who was living in Venezuela 5 years ago. There is extensive variation in these migrant shares across Colombia. They tend to be largest closer to the Venezuelan border, in many cases exceeding 10% of the metro area population. In Cúcuta and Riohacha, two cities close to the primary entry points along the Venezuelan border, the migrant shares are around 16% and 11%, respectively. In Bogotá, Medellín, and Cali, the three largest cities in Colombia, the shares range between 4% and 5%. For other cities, they remain below 1%.

Figure 2

The majority of migrants crossed at a handful of official border crossings, which required a passport or a visa that allowed for short-term access to the border regions. However, those without legal documents could pass around border checkpoints on paths commonly known as “trochas”. The Colombian government created a temporary resident visa beginning in January 2017 (the Permiso Temporal de Permanencia [PEP]), which allowed documented migrants to access the formal labor force and additional education and health services. This status was offered to a large number of undocumented migrants starting in April 2018 through a process called the RAMV. This was intended to regularize the growing number of migrants who had either entered illegally or overstayed their temporary permit (the Registro Administrativo de Migrantes Venezolanos [RAMV]). By the end of 2019, according to official numbers from the Colombian migration authorities, an estimated 754,000 Venezuelan migrants were regularized, corresponding to approximately 42% of the Venezuelan migrants estimated to be in the country (Migración Colombia, 2019). Furthermore, Bahar et al. (2021) show that the 2018 RAMV regularization had little-to-no effect on native labor outcomes, likely because registered migrants mostly remained in the informal sector. In summary, there was little control over who entered the country and where migrants went within Colombia, and despite many having access to regularization, the majority of migrants remained undocumented and informal. Both documented and undocumented migrants are included in my data and I do not observe documentation status.

Another important characteristic of this migration wave is that, unlike with many other global episodes of forced displacement, relatively little international aid has been dedicated to the reception of Venezuelan migrants. By 2019, international funding for the Venezuelan migration crisis was at $580 million, compared to $7.4 billion that went to displaced Syrians in the first 4 years of the Syrian crisis (Bahar and Dooley, 2019). Furthermore, few migrants are living in camps, and the Colombian government has been unable to mobilize large-scale aid or investment into areas most affected by migration (Migration Policy Institute, 2020).

Migration can also affect local economies by increasing local consumer demand, especially if migrants carry savings (Verme and Schuettler, 2021; Cortes, 2008). However, it is estimated that Venezuelan migrants’ household expenditures in Colombia are less than half that of natives, reflecting migrants’ low income in Colombia and the fact that savings for many Venezuelans was wiped away by inflation (Tribín-Uribe et al., 2020). Delgado-Prieto (2021) studies the effect of migration on the consumer price index across 23 capital cities in Colombia and finds precise null effects, though there is evidence for small increases in the cost of education and small decreases in the cost of health care. Overall, the demand effects of migration in this context appear to be modest, and I do not study the effects on prices in this paper. The literature would benefit from a more detailed analysis of the effect of Venezuelan migration on the local prices of different goods and services. To the extent that increased demand directly affects wages, this will be captured in the estimated wage effects.

Labor market outcomes come from the GEIH, which is a large-sample cross-sectional survey collected by the National Administrative Department of Statistics (Departamento Administrativo Nacional de Estadística [DANE]) and is the official source for labor market indicators in Colombia. Since 2013, this survey has included a migration module that can be used to identify migrants, and I therefore also use this survey to measure migration shares across regions and over time. This module also allows me to restrict labor market outcomes to nonmigrants, to avoid any compositional effects driven by arriving migrants.

It is important to note that the GEIH is not intended to be representative of Venezuelan migrants in Colombia. Another potential source of the migrant share across regions is the 2018 census, but this comes with two caveats.

Another possible source is the official estimate from the Colombia Migration Unit, which is imputed based on a combination of border flows, registration of undocumented Venezuelans, and the 2018 census. However, these numbers likely undercount undocumented migrants, especially before 2018 and in locations farther from the border (Tribín-Uribe et al., 2020; Graham et al., 2020).

I define migrants as anyone who was living in Venezuela 5 years ago. Importantly, this includes Colombian-born return migrants, who make up around 20% of all migrants from Venezuela during this period. Many of these returnees migrated to Venezuela during Colombia’s decades-long civil war. They are on average older and less educated than Venezuelan-born migrants, and there are various reasons to believe that their effect on the labor market may differ.

In the working-age metro sample of the 2019 GEIH, the average age of return migrants and Venezuelan-born migrants is 38.7 years and 30.0 years, respectively. The completed years of schooling is 8.2 years and 10.4 years, respectively.

Colombia is divided into a capital district and 32 departments, which are further divided into 1,122 municipalities. In order to generate a geographic unit that represents a contiguous labor market in which workers compete, I group municipalities into metropolitan areas according to commuting patterns. Following Duranton (2015), I use a recursive algorithm based on a 10% commuting threshold using commuting data from the 2005 census, which is the latest year before the start of the migration period in which such data are available.

Specifically, a municipality is grouped with another if >10% of its residents commute to work in that municipality. They are then treated as a single unit in the next round of the algorithm, and this is repeated until no more municipalities meet this threshold. In practice, the number of metro areas generated by this method does not depend on the choice of commuting threshold. See Duranton (2015) for details.

A concern about measurement error arises when the GEIH is used at such a fine geographic level, since it is only designed to be representative at the level of the department or the 23 official metro areas. I address this in various ways. First, I restrict analysis to the 79 metro areas that contain at least 300 observations per year. These represent around 80% of the Colombian population and 90% of the Venezuelan migrant population. Second, I test the robustness of results to increasing the annual observation threshold to 1,000, essentially restricting analysis to the 23 metro areas for which the survey is officially representative.

Third, in my analysis, I use an instrument based on migration shares from the complete 2005 National Census, which will mitigate the effect of measurement error in the endogenous variable. Finally, I test robustness to using alternative geographic units (including the department level) in Section 7, and I find that choice of geographic unit only has a moderate effect on the results.

I now describe the characteristics of working-age (15–64) migrants and natives in the 79 metro areas of analysis in the 2019 GEIH using sampling weights, which has a national sample of 447,264 natives and 21,730 migrants. Table A1 shows that migrants are gender balanced and 5 years younger than natives on average. Figure A1 shows that migrants come most heavily from the middle of the education distribution: 44% have completed secondary education relative to 35% of natives. However, >20% of migrants have some postsecondary education, indicating that this is not a low-skill migration wave, and the educational profile of migrants and natives is broadly similar. However, by plotting the distribution of migrants and natives across occupations ranked according to mean years of completed schooling for natives, Figure A2 shows that the majority of migrants are concentrated in occupations that tend to employ less-educated natives.

Occupations are recorded in the GEIH using the 82 classifications of the 1968 International Standard Classification of Occupations (ISCO-68). They are ranked by the average years of schooling for natives between 2010 and 2015.

I estimate the following regression across metro areas (c) and years (t) from 2014 to 2019: (3) Yct=βMct+γc+δt+εct {Y_{ct}} = \beta {M_{ct}} + {\gamma _c} + {\delta _t} + {\epsilon _{ct}} where M_ct is the migrant population as a share of the 2014 population. Metro fixed effects, γ_c, hold constant all time-invariant metro characteristics; year fixed effects, δ_t, adjust for national-level changes in labor outcomes. Standard errors are clustered at the metro level to allow for the error to be correlated within metro areas over time, and observations are weighted by the population within each metro–year cell.

I choose not to use the GEIH sampling weights since they are not designed to be representative at this level, but my results are not sensitive to this decision.

Labor market outcomes, Y_ct, are averaged at the metro–year level and include labor force participation, unemployment, hours worked in a typical week, and log hourly wage, including all overtime, benefits, and other transfers. This information is collected for all workers regardless of self-employment or formality status, and going forward, I use hourly wage to refer to hourly earnings for wage workers or hourly profits for self-employed. These outcomes are residualized from a regression on gender, age, and education fixed effects, though this adjustment has little effect on the results.

Age is grouped into 5-year intervals, and education is grouped into less than primary, less than secondary, completed secondary, and postsecondary.

There has been recent concern regarding bias in two-way fixed-effect models when there are dynamic treatment effects (Callaway and Sant’Anna, 2021; Goodman-Bacon, 2021; Borusyak and Jaravel, 2021; De Chaisemartin and d’Haultfoeuille, 2020). Intuitively, in two-way fixed-effect models, groups that are “treated” later in the study period use previously treated groups as a control, even though they may still be experiencing a dynamic treatment effect. While these papers generally deal with models that have a binary treatment, the same concern in principle extends to a continuous treatment framework.

One paper, by De Chaisemartin and d’Haultfoeuille (2020), develops an estimator robust to heterogeneous treatment effects, which works with a nonbinary treatment. However, it only extends to discrete treatments (as opposed to continuous) and is not identified when treatment takes too many values. When I apply the estimator developed in this paper with migrant shares grouped into intervals, the resulting confidence intervals are not informative.

One cannot simply compare labor market outcomes in metro areas that experienced different migration levels because migrants select destinations according to endogenous characteristics. For example, if migrants are more likely to settle in cities with greater expected growth in available jobs or wages, this would induce a positive correlation between ∊_ct and M_ct and an upward bias in the estimate of β. I deal with this endogeneity by constructing the following instrument: (4) Zct=Mc,2005×MNat,t−c {Z_{ct}} = {M_{c,2005}} \times M_{Nat,t}^{ - c} where M_c,2005 is the 2005 Venezuelan share of the population in metro area c according to the complete 2005 population census, and MNat,t−c M_{Nat,t}^{ - c} is the “leave-one-out” national share of migrants from Venezuela to all metro areas in year t, excluding migration into area c (Card, 2001; Tabellini, 2020). This “leave-out” factor reduces the correlation between national-level inflows and large inflows into certain cities, which may be correlated with time-changing characteristics of those cities.

This variable is strongly predictive of subsequent migrant shares, creating the strong first stage needed for consistent two-stage least squares (2SLS) estimates. Figure A3 displays the positive linear relationship between the 2005 Venezuelan share (which ranges from 0% to 0.9%) and the 2019 migrant share (which ranges from 0% to 25%). There is strong persistence over time in the distribution of Venezuelan migrants across metro areas, likely driven by the tendency of migrants to locate where they have migrant networks (Beaman and Magruder, 2012; McKenzie and Rapoport, 2007; Munshi, 2003). When the instrument in Eq. 4 is used with metro and year fixed effects, the first-stage Kleibergen-Paap (K-P) Wald statistic is 23.

The Kleibergen-Paap Lagrange multiplier (LM) test tests the null hypothesis that the structural equation is underidentified. With a single endogenous regressor, this reduces to a standard first-stage F-statistic that is heteroskedasticity robust.

The variable MNat,t−c M_{Nat,t}^{ - c} is assumed to be exogenous, driven primarily by push factors in Venezuela, and uncorrelated with any changes occurring in Colombia. Unemployment in Colombia steadily increased from 8.5% to 10% from 2014 to 2019, indicating that there were no favorable labor market conditions attracting migrants over this period. Furthermore, migration did not increase from any other country. Of greater concern is the potential endogeneity of M_c,2005, which may be correlated with changes in economic outcomes between 2014 and 2019 in metro area c through channels other than the mass migration. This concern is mitigated by the fact that historical migrant shares were determined 2 decades before the onset of the Venezuelan exodus, well before the election of Hugo Chávez. While I use the 2005 census to construct the instrument, I show that results using the 1993 census are similar. The correlation between the migrant shares in these years is 0.89.

I prefer to use the 2005 census to construct the instrument because I have access to the complete census for this year, which helps to minimize measurement error.

It remains possible that, between 2014 and 2019, migrants historically selected and moved into cities that had differential economic trends. While this cannot be formally tested, I conduct various checks and robustness tests recommended by the literature (Goldsmith-Pinkham et al., 2020). First, I check for a correlation between the 2005 shares and the preperiod economic outcomes. Table A2 shows a regression of the 2005 Venezuelan share on a set of metro area characteristics measured in 2014, before the onset of the migration. The results show that a 1% increase in wages is associated with a 0.02 standard deviation (SD) decrease in the 2005 migrant share. Hours, labor force participation, unemployment, and total population are all insignificant and small in magnitude. Importantly, the value of R² is small, indicating that only 9% of the variation in the 2005 migrant share can be explained by all of these variables together. The largest concern is that places with more immigration in 2005 had slightly lower wages in 2014.

These fixed metro characteristics are controlled for in the analysis. It is arguably more relevant to test whether historical migrant shares are correlated with pre-trends in economic outcomes leading up to the migration. I run the following event-study model: (5) Yct=∑y=20102014[σyMc,2005*(t=y)]+∑y=20162019[σyMc,2005*(t=y)]+γc+δt+εct {Y_{ct}} = \sum\limits_{y = 2010}^{2014} {\left[ {{\sigma _y}{M_{c,2005}}*\left( {t = y} \right)} \right]} + \sum\limits_{y = 2016}^{2019} {\left[ {{\sigma _y}{M_{c,2005}}*\left( {t = y} \right)} \right]} + {\gamma _c} + {\delta _t} + {\epsilon _{ct}} where σ_y measures the differential change in the outcome for cities that had a relatively higher 2005 migration share (in SDs) relative to the excluded year of 2015, the year preceding the onset of the migration. The 95% confidence interval (CI) around the coefficient for each primary outcome is presented in Figure A4. Hourly wages show a decreasing trend from 2011 to 2013, but this levels off and is flat in the 2 years before the migration. After 2015, it drops precipitously, in line with the 2SLS results. Hours per week is stable in the preperiod and increases after 2015, also consistent with the 2SLS results. However, pre-trends are observed for unemployment rates (which increase steadily during the preperiod and then flatten after the migration) and participation rates (which decrease between 2013 and 2014 and again after the migration). This motivates an adjustment for pre-trends when using this instrument to study unemployment and participation, which I include as a robustness check.

Various papers (Caruso et al., 2021; Delgado-Prieto, 2021; Bonilla-Mejía et al., 2020; Santamaria, 2020; Penaloza-Pacheco, 2021) have also studied the effects of Venezuelan migration to Colombia on native employment and earnings. While they are generally consistent in finding null or small employment effects and negative wage effects for natives, the magnitude of the estimated wage effect varies drastically, with elasticities ranging from −0.5% to −7.5% from a 1 pp increase in the migrant share. This variation could be driven by various specification choices, including the geographic unit of analysis, the instrument, and the formula and data used to measure the migrant share of the population. In this section, I explore the sensitivity of the magnitude of the wage effect to these factors, to explain the dispersion in the literature and to shed light on the specification choices that may be most consequential when estimating the economic effects of migration.

In Table A3, I start by cross-interacting three dimensions of sensitivity: the chosen instrument, the geographic unit of analysis, and whether or not return migrants (born in Colombia and living in Venezuela before the migration) are included in the migrant share. The first dimension that I vary is the choice of instrument. Table A3 shows that the OLS model consistently generates smaller wage effects, consistent with migrants positively sorting into high-wage locations. This already helps to explain some variation in the literature: the papers that report smaller coefficients of −0.5, viz., Penaloza-Pacheco (2021) and Santamaria (2020), use OLS and thus do not account for migrant positive sorting.

The goal of this analysis is not to fully replicate the coefficients from each paper. There remain differences in how variables are calculated and analysis is conducted across papers. For example, Santamaria (2020) uses Google search keywords to measure migrant locations across departments. The goal is instead to identify the factors that explain the variation in results.

The papers that use 2SLS differ in their choice of the “share” component of the shift-share IV, using either historical migrant shares based on the 1993 or 2005 census or the inverse driving distance to the Venezuelan border.

Distance to the border can be replaced with a summed distance to each Venezuelan department weighted by the share of Colombian expatriates living in each department (Caruso et al., 2021; Delgado-Prieto, 2021). Here, I simply use driving distance to the border, which is closely correlated with this measure. Driving distance is calculated using Open Street Maps, from the central municipality of the metro area to the closest Venezuelan border crossing. I continue to use the “leave-out” instrument, which does not affect results.

Second, these papers differ in their unit of analysis, either at the level of the 24 departments or 23 administrative metro areas. The primary advantage of conducting analysis at these levels, relative to the 79 commuting-zone (CZ)-based metro areas that I construct, is the mitigation of measurement error concerns since the GEIH is representative at these levels.

The disadvantage is that departments are large while most migrants are located in cities, and the official metropolitan areas are somewhat arbitrarily defined according to political considerations (Duranton, 2015). Table A3 shows that the wage effect tends to be smaller at the administrative metro area level and biggest at the department level, but results are generally similar across these specifications.

The instrument is also adjusted to calculate both the historical shares and the national shift at each geographic level. Distance to the border for departments is calculated from the department capital.

Third, not all of these papers choose to include Colombian return migrants when calculating migration shares. Table A3 thus shows that the coefficients are inflated when return migrants are excluded. The coefficient increases from −1.05 to −1.24 in the baseline specification and further to −1.48 using the distance IV at the department level. As discussed, Venezuelan-born and return migrant shares are correlated. Therefore, to exclude return migrants from the migrant share is to assume that they have no effect on local labor markets and to attribute any changes in the labor market outcomes to the Venezuelan-born migrant population. While it is possible that the increased effect size of −1.24 is driven by a larger effect of Venezuelan-born migration on wages, it is equally likely that it is driven by omitted-variable bias, which will have a drastic effect on the estimated magnitude. To see this, consider the framework outlined in Section 1. A regression of the foreign-born migrant share (predicted by the instrument) on the return migrant share with metro and year fixed effects generates a coefficient of 0.2. Thus, if the effect of Venezuelan-born migration and return migration are both −1.05, one would expect a coefficient of −1.26 [since −1.05 – (1.05 × 0.2) = −1.26], very close to the observed result. It would also be possible for the effect of Venezuelan-born migration to be −1.1 and of return migration to be −0.7 [since −1.1−(0.7 × 0.2) = −1.24], or for the effect of Venezuelan-born migration to be −0.9 and of return migration to be −1.7 [since −0.9−(1.7 × 0.2) = −1.24] Thus, a range of possible effects are consistent with the observed change in magnitude, including scenarios in which Venezuelan-born migration has a larger or smaller effect than return migration.

Delgado-Prieto (2021), using a specification in which the change in outcomes relative to the baseline period is regressed on the 2018 migrant share, finds a significant wage elasticity of −1.7. An important difference in this paper is the use of the 2018 census to calculate migration rates. As discussed in Section 4, there are two caveats with the census: it undercounts the Colombian population by 8.5%, and it only measures migration in the first three quarters of 2018. Given that the GEIH is also not designed to be representative of the migrant population, it is not obvious a priori whether one is more desirable than the other. However, the fact that the GEIH can measure the migration rates in other years, rather than only in 2018, is a large advantage. To test sensitivity to the choice of data set, I run this specification using both the GEIH and the census to measure the migrant share in 2018.

There are a few additional changes in how I use the GEIH in this specification so as to allow the results to be comparable with those estimated using the 2018 census. First, the migrant share includes migrants from all countries as opposed to only those from Venezuela. This is because the census does not ask for country of origin. However, this does not add very much noise because, according to the GEIH, 95% of foreigners who arrived over this period came from Venezuela. Second, the migrant share is taken as a fraction of the current population rather than the 2014 population, and again, this does not have a large effect on results.

First, the analysis shows that, using a 2014–2018 difference model and using the GEIH to measure the migrant share, the results are very similar to the baseline specification. Second, once the 2018 census is used to measure the migrant share, the wage effect magnitude increases by around 20%, and this is true using each instrument and geographic unit of analysis. Thus, if we believe that the census is a more accurate measure of migrant locations, then the true wage effect becomes slightly larger, to −1.26 in the baseline specification. However, this is still not large enough to reconcile the primary results from Delgado-Prieto (2021): using the department unit (as in the paper), the wage coefficient ranges from −1.36 to −1.53 depending on which instrument is used.

The remaining difference in this paper’s specification that explains the larger coefficient is the exclusion of return migrants in the migrant share, which – as we have seen – further inflates the wage coefficient. This is presented in Panel B of Table A4, where using the 2018 census, the 2SLS wage coefficient now ranges from −1.46 to −1.77 using CZ metro areas. At the department level, it ranges between −1.72 and −2.02. To conclude, the large coefficient found in Delgado-Prieto (2021) is not driven by stopping the analysis in 2018. It can be explained by a combination of using the 2018 census rather than the GEIH and, more importantly, excluding return migrants from the migrant share. If the reader’s preferred specification is to measure total migration with the 2018 census using the migrant enclave IV, then the proper coefficient is between −1.09 and −1.13 using the administrative metro areas, between −1.21 and −1.26 using the CZ metro areas, or between −1.32 and −1.36 at the department level.

Another result unique to Delgado-Prieto (2021) is the large estimated negative employment effect of −1.7% from a 1 pp increase in the migrant share. Using log total employment as the outcome in my primary specification, I find an insignificant negative effect of −0.2. However, this increases to −0.7 using the distance IV and increases further to −1.5 when data are restricted to the year 2018. This is consistent with Delgado-Prieto (2021)’s result that the employment effect of −1.7 coinciding with the 2018 migrant surge remains unchanged and, in fact, diminishes in 2019, despite large numbers of migrants continuing to arrive.

A final paper is by Caruso et al. (2021), which finds a negative wage effect of −7.6% from a 1 pp increase in the migrant share, almost five times larger than the estimate by Delgado-Prieto (2021). One difference in this paper is that their analysis ends in 2017, before the majority of migrants arrived. They also conduct analysis at the department level combined with an inverse border distance instrument, which – we have seen – tends to generate a larger wage effect. However, the most consequential difference is that they define the migrant share as the share of the population that arrived from Venezuela over the past 1 year, rather than 5 years. Similar to the case of excluding return migrants, this will generate omitted-variable bias considering that these shares are highly positively correlated, and this will inflate the wage effect if previously arrived migrants also have a depressing effect on wages. In this example, this is also akin to using a migration flow rather than a migration stock on the right-hand side.

According to the GEIH, only 0.23% of the population had come from Venezuela in the past 5 years in 2014. Thus, using the 5-year migration measure until 2019 essentially measures the stock of migrants in the country who arrived since 2014.

In Table A5, I run the baseline specification using the migrant share defined in terms of 1-year flows, and I do this both through the full period and using data only through 2017 to test sensitivity to the period of analysis. The 1-year flow estimates are substantially larger across all specifications. In the baseline specification, the wage coefficient increases to −3.53.

Returning again to the framework in Section 1, this would be consistent with, for example, 1-year and 5-year migrations having an effect of −1.5 and −0.8, respectively, considering that the regression of the predicted 5-year share on the 1-year share generates a coefficient of 2.5, and −1.5 −(0.8 × 2.5) = −3.5.

To conclude, differences in these specification choices are able to explain the variation in the average wage effect reported in the literature. Choice among the candidate instruments and geographic unit of analysis leads to small differences in magnitudes, while choices relating to the measure of the migrant share are most consequential: when the migrant share is restricted to only a portion of the migrant population, or to those who arrived within the past year, the wage effect is substantially inflated. When the 2018 census is used to measure migration through 2018, the predicted wage effects also increase slightly. It is worth noting that, while the magnitude of the wage effect varies substantially, most of these papers find that the wage effect is larger for less-educated natives.

Armed with a preferred specification that uses an instrument based on historical migrant shares, variation across CZ metropolitan areas, and measuring the total migrant share using the GEIH, I now conduct various additional robustness tests for all four labor market outcomes, for the population average and by education group. The most important result from this section is that, after controlling for region-specific time trends, the wage effect falls to −0.59.

I start by testing whether proximity to the Venezuelan border is a relevant omitted variable, since it is correlated with both the 2019 and historical migrant shares. In particular, cities very close to the border have experienced changes over this period in economic activity, commuting flows from Venezuela, and violent crime (Knight and Tribin, 2020). The cities with the highest migrant shares, including all of those with a migrant share >15%, are located within 100 km driving distance from the Venezuelan border. To ensure that these cities are not driving the results, I drop these six cities in Column 2 of Table 3. The instrument loses power (the first-stage Wald statistic falls to 13), and standard errors increase substantially. However, the coefficient values remain stable overall and within education group, implying that wage effects are not driven by these six metro areas. Effects on labor force participation, on the other hand, are eliminated when these cities are excluded.

Proximity to the Venezuelan border may remain an omitted variable if, among cities with distances of >100 km from the border, those closer to the border experienced decreases in trade with Venezuela over this period. While Venezuela used to be a top trading partner of Colombia, its trade shares steadily declined during the 2000s such that it represented a small share of imports and exports by 2010. However, trade persisted longer for departments closer to the border. In Column 3, I therefore control for total imports and exports with Venezuela at the department level, and the results are highly robust.

Trade data were downloaded from DANE and measure the net weight of all Venezuelan imports and exports with origin or destination in each department.

To more flexibly account for distance to the border, I control for a linear trend interacted with inverse driving distance to the border. When I do this in Column 4, the estimated average wage elasticity falls to −0.53, but the first-stage F-statistic becomes weak and the standard error increases drastically, such that the coefficient is not statistically different from the original specification. I conclude that it is not feasible to isolate variation in the predicted migrant share from this distance measure. Thus, it remains possible that 2SLS results are partially explained by trends associated with border proximity.

In all robustness checks with a linear trend, I can instead use interactions with year fixed effects, and results are qualitatively similar, though the standard errors are less precise. I can also use linear distance instead of driving distance, and results are similar. These are available upon request.

Considering this, another method to control for unobserved heterogeneity across broad geographic areas is to control for linear trends interacted with fixed effects for the four regions of Colombia defined by DANE: Pacific, Caribbean, Central, and Eastern, the last of which incorporates Bogotá. Accounting for regional time trends was also found to be important in the case of Syrian migration to Turkey (Aksu et al., 2018). The region dummies are interacted with a time trend rather than year fixed effects to preserve power in the first stage. The results in Column 5 show that the wage effect is mitigated to −0.59 and remains statistically different from zero, though it is again not statistically different from the baseline estimate. This indicates that part of the 2SLS wage effect is driven by regional time trends, and after controlling for them, the true wage effect decreases. None of the papers discussed in Section 7 complete this robustness check. If I estimate the model using the 2018 census to measure migration as in Column 2, Row 2 of Table A4, addition of region fixed effects brings the coefficient down from −1.26 to −0.70.

It is also notable that the wage effect for less-educated natives decreases the most when region trends are included, but the standard errors also increase the most, such that the effect for the less-than-secondary group is not significantly different from the baseline estimate and includes a wide range of plausible estimates. Thus, we are unable to isolate the effect from region trends for this subgroup.

Next, motivated by the presence of pre-trends in unemployment and participation, in Column 6, I interact a linear year trend with the change in the outcome between 2013 and 2015, allowing linear changes over the migration period to vary flexibly with preperiod trends. As expected, this has little effect on the wage and hour estimates. Despite potential pre-trends for unemployment, the unemployment coefficients remain stable. The negative coefficient on participation decreases in magnitude and becomes insignificant for each education group, implying that the small decreases in participation are partially driven by trends that began before the Venezuelan exodus. This is consistent with evidence from Delgado-Prieto (2021) that native employment effects are mitigated after accounting for pre-trends.

Finally, in Table A6, I conduct various checks that have no effect on the estimated coefficients. First, I drop Bogotá, which is the largest city in the sample, to ensure that it is not disproportionately driving results.

I can also drop all metro areas one by one, and this is available upon request.

The migration from Venezuela to Colombia presents a unique opportunity to better understand the short-term effects of mass migration on native labor market outcomes in a developing country and in a context where natives and migrants share a similar culture and language. The results show little effects on the employment margin: there was a small decrease in participation and increase in school attendance among people younger than 25 years of age, but this was driven entirely by cities close to the Venezuelan border and was mitigated after adjusting for pre-trends. However, there were negative and robust effects on native hourly wages most pronounced for informal and less-educated workers, consistent with low reservation wages and high wage flexibility. These results are not biased by the small increase in native internal migration that occurred in response to the Venezuelan arrival, or by the small shifts in occupational skill group that benefited some workers and harmed others. They are consistent with a pattern in the literature in which the economic consequences of migration are most pronounced in developing countries, especially for less-educated and informal workers, and clearly motivate policy responses to mitigate the economic consequences of migration. They also motivate additional research to better understand the drivers of these economic consequences in developing countries. That these wage effects are moderately stronger in metro areas with higher baseline informality rates and lower ease of starting a business indicates that local economic conditions are a determinant of the labor market effects of migration and motivates the formulation of policies to facilitate business formation or encourage migrant relocation according to local economic conditions. The role of migrants’ occupational downgrading is explored extensively by Lebow (2022), and the results indicate that migrant downgrading plays an important role in concentrating wage effects among lower-income natives.

The robustness and sensitivity analysis identified two important caveats for the estimated average native wage effect of −1.05% from a 1 pp increase in the migrant share. First, when the 2018 census rather than the GEIH is used to measure the migrant share, the magnitude of the average wage effect increases to −1.26%. Second, after controlling for regional time trends, the wage effect decreases to −0.59% (or −0.70% using the 2018 census), with a 95% CI ranging from [−1.14, −0.04].

Finally, I demonstrated the specification choices that explain the variation in estimated wage effects in the literature studying Venezuelan migration to Colombia. The papers that find small or insignificant wage effects do not use an instrument and thus fail to account for the positive sorting of migrants into favorable locations. Larger wage effect magnitudes of −1.7% and −7% found in the literature are only partially explained by differences in the instrument, geographic unit, time period of analysis, or data used to measure migration. The most important determinant is that, when a subset of the migrant population is excluded from the migrant share or when the migrant share is defined to only include recently arrived migrants, the wage effect is inflated substantially. This is likely driven by omitted-variable bias and presents an important lesson for migration researchers.