The labor market effects of Venezuelan migration to Colombia: Reconciling conflicting results
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Lebow, Jeremy Article The labor market effects of Venezuelan migration to Colombia: Reconciling conflicting results IZA Journal of Development and Migration Provided in Cooperation with: IZA – Institute of Labor Economics Suggested Citation: Lebow, Jeremy (2022) : The labor market effects of Venezuelan migration to Colombia: Reconciling conflicting results, IZA Journal of Development and Migration, ISSN 2520-1786, Sciendo, Warsaw, Vol. 13, Iss. 1, pp. 1-49, https://doi.org/10.2478/izajodm-2022-0005 This Version is available at: https://hdl.handle.net/10419/298714 Standard-Nutzungsbedingungen: Die Dokumente auf EconStor dürfen zu eigenen wissenschaftlichen Zwecken und zum Privatgebrauch gespeichert und kopiert werden. Sie dürfen die Dokumente nicht für öffentliche oder kommerzielle Zwecke vervielfältigen, öffentlich ausstellen, öffentlich zugänglich machen, vertreiben oder anderweitig nutzen. Sofern die Verfasser die Dokumente unter Open-Content-Lizenzen (insbesondere CC-Lizenzen) zur Verfügung gestellt haben sollten, gelten abweichend von diesen Nutzungsbedingungen die in der dort genannten Lizenz gewährten Nutzungsrechte. Terms of use: Documents in EconStor may be saved and copied for your personal and scholarly purposes. You are not to copy documents for public or commercial purposes, to exhibit the documents publicly, to make them publicly available on the internet, or to distribute or otherwise use the documents in public. If the documents have been made available under an Open Content Licence (especially Creative Commons Licences), you may exercise further usage rights as specified in the indicated licence. https://creativecommons.org/licenses/by/4.0/
Jeremy Lebow* The labor market effects of Venezuelan migration to Colombia: reconciling conflicting results† Abstract The recent mass migration of Venezuelans to Colombia has become a focal point for economists interested in the labor market effects of migration in developing countries. Existing papers studying this migration wave have consistently found negative effects on the hourly wages of native Colombians, which are most concentrated among less-educated natives working in the informal sector. However, the magnitude and significance of this wage effect varies substantially across papers. I explore the potential specification choices that drive this variation. Differences in how migration is measured are particularly important: exclusion of a subset of migrants from the migration measure, according to characteristics such as time of arrival, amounts to an omitted-variable bias that will tend to inflate the estimated wage effect. In my own analysis based on the total migration rate across 79 metropolitan areas and by using an instrument based on historical migrant locations, I estimate a native hourly wage effect of −1.05% from a 1 percentage point increase in the migrant share or an effect of −0.59% after controlling for regional time trends, alongside little-to-no effect on native employment. Native movements across occupation skill groups and geography are small and do not play a meaningful role in mitigating local wage effects. Wage effects are also larger in cities that have a higher baseline informality rate and lower ease of starting a business. Current version: February 17, 2022 Keywords: immigration, labor markets, informality JEL codes: F22, J21, J46 Corresponding author: Jeremy Lebow [email protected] Lebow. IZA Journal of Development and Migration (2022) 13:05 © The Author(s). 2022. Open Access This article is distributed under the terms of the Creative Commons Attribution 4.0 International License (http://creativecommons.org/licenses/by/4.0/), which permits unrestricted use, distribution, and reproduction in any medium, provided you give appropriate credit to the original author(s) and the source, provide a link to the Creative Commons license, and indicate if changes were made. Cite as: Lebow. IZA Journal of Development and Migration (2022) 13:05 https://doi.org/10.2478/izajodm-2022-0005 Department of Economics, Duke University, 213 Social Sciences, Durham, N.C. 27708 † This paper was previously circulated under the title “Refugees in the Colombian Labor Market: The Consequences of Occupational Downgrading”.
Page 2 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 1 Introduction 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).1 Furthermore, around 25% of natives and 30% of migrants are self-employed own-account (with no employees) workers and, thus, compete directly over prices. Second, Venezuelan migrants and Colombian natives speak the same language and have a similar cultural background, which increases their substitutability in the workforce (Braun and Mahmoud, 2014). This also limits the scope for natives to respond to migration by upgrading to communication-intensive tasks (Peri and Sparber, 2009; Peri et al., 2020). Third, Colombia has experienced extensive internal migration from decades of civil war and has an unemployment rate that has hovered between 8% and 11% since 2010, indicating limited capacity to mobilize capital to absorb an expanding workforce (Calderón-Mejía and Ibáñez, 2016; Morales, 2018). Finally, an important characteristic of this migration is the occupational downgrading of migrants: while Venezuelan migrants and Colombian natives have similar levels of education, Venezuelan migrants are heavily concentrated in occupations, such as restaurant work, construction, street vending, and domestic service, which typically require less education. Because migrants in Colombia 1 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.
Page 3 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 are mostly competing with less-educated workers in the informal sector, we expect economic effects to be most concentrated among these natives, with potential benefits for more-educated natives (Dustmann et al., 2013). 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 25years 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).2 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 1pp increase in the migrant share.3 I show that the 2 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. 3 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.
Page 4 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 smaller estimates can be explained by failing to use an instrument to account for the endogenous sorting of migrants into locations, which biases the estimated wage effect toward zero. I show that among the various factors that explain the larger estimates, the most important is related to implicit assumptions made while calculating the migrant share of the population. Specifically, by restricting migration to include only those who arrived over the past 12months or by excluding Colombian-born return migrants, the estimated wage effect become substantially inflated due to what I argue is best understood as omitted-variable bias.4 This is because the location of previously arrived migrants (or return migrants) is strongly correlated with that of recently arrived migrants (or Venezuelan-born migrants), and it is reasonable to expect that both groups affect the local economy. To illustrate this concept, let “M1” represent the share of the population of migrants who arrived in the past 12months, and let “M5” represent the share who arrived in the past 13–60months. Regress the average native log-wage in region k and year t on M1kt with region and year fixed effects5: = +++ln 1 kt kt k t kt WM β γδ (1) Assume M1kt and kt are uncorrelated conditional on the fixed effects. Let the true effect of M1kt and M5kt on lnWkt be α1 and α5, respectively. Then, β, the marginal effect of M1kt on lnWkt (suppressing conditionality on the fixed effects from the notation for brevity), is obtained as follows: 15 ln 5 ˆ 11 kt kt kt kt WM MM ∂∂ = =+ ∂∂ β αα (2) Thus, excluding M5kt from the regression generates an omitted-variable bias equal to 5 1 5 kt kt M M ∂ ∂ α . 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 M1kt, in which case, M1kt can be replaced with 1kt M 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 M5kt on the predicted 1kt M and year and metro area fixed effects generates a coefficient of 2.6, such that even a small value of α5 will substantially bias ˆ β . 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 ˆ β =3.5 [since −1.5 – (0.8×2.6)=−3.5], much larger than the true α1 of −1.5. As I will show, this is the estimate of ˆ β 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 4 Return migrants are those who were born in Colombia, migrated to Venezuela in the decades preceding the Venezuelan crisis, and then returned to Colombia during the crisis. They make up around 20% of migrants who arrived from Venezuela between 2014 and 2019. 5 The fixed effects are not necessary for this exercise, but I have included them to match the typical specification in the literature.
Page 5 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 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 M1kt and M5kt 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 M1kt and M5kt. 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.6 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-re- ported 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. 6 Note that it is not satisfactory to simply use an instrument for one group, M1kt, while controlling for the other, M5kt. If M5kt is correlated with the instrument and the error term, this is an “endogenous controls” problem and βb 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 M5kt, but this is demanding and requires extensive independent variation in the endogenous variables.
Page 6 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 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 policymakers 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. 2 Literature 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 10years. 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 4–7years (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 5years. 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
Page 7 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 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.7 In contrast, Fallah et al. (2019) find no economic effects of Syrian refugees in Jordan, potentially explained by low refugee labor force participation alongside increases in EU aid and trade concessions. 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).8 In Brazil, migration is found to affect participation rather than wages when using a synthetic control method (Ryu and Paudel, 2022). Papers have also highlighted migrant occupational downgrading as a mechanism behind the unequal wage effect in Colombia: Lebow (2022) estimates a production function that allows for imperfect substitutability between migrants and natives and finds that migrant occupational downgrading led to increases in the wage effect for less-educated natives, alongside decreases in total productivity. Lombardo et al. (2021) also show that the magnitude of the negative wage effect is increasing in the density of the migrant share along the native wage distribution. Finally, there are studies of the labor market consequences of internal displacement during Colombia’s civil war between the 1980s and the early 2000s. These papers have found negative wage effects for urban workers ranging from −0.09% to −1.4%, which are consistently larger for low-skill and informal workers (Calderón-Mejía and Ibáñez, 2016; Morales, 2018). My results are consistent with these estimates. 3 Background on Venezuelan Migration 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). 7 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). 8 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.
Page 8 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 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 2015.9 The arrival rate increased in 2016 and again in 2017, with the majority of migrants arriving between 2018 and 2019. The results presented in this paper therefore reflect very short-run economic effects. 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 5years 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%. 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 9 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 Foreign-born population in Colombia. Sources: Colombian National Integrated Household Survey (GEIH) (2013–2019); Population Census (1993, 2005).
Page 15 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 of the migrant share across metro areas in 2019 (from 1% to 8.6%) is associated with a 7.98% decrease in wages. This effect is economically meaningful, considering that average wages for natives in the sample increase by around 4% over the period 2014–2019. That the 2SLS is more negative than the OLS indicates that there was positive selection of migrants into locations that had bigger increases in wages, though this difference is not significant according to a Hausman test for endogenous regressors. There is little effect on hours or unemployment, and a small negative effect is found on participation, which is significant at the 10% level. Specifically, a 1pp increase in the migrant share causes a 0.21pp decrease in labor force participation, with a 95% CI that includes [−0.43, 0.01]. This is associated with a 1.6pp decrease in participation from the 10th percentile to the 90th percentile of the migrant share, relative to a 2014 sample mean of 72.6%. Thus, the majority of the effect on natives was seen on the earnings margin rather than on the employment or participation margin. In Table 2, I split the outcomes by gender, age, and education.21 The results show that the effect on wages is slightly stronger for men, though the difference is not significantly significant. Though there are various examples of female participation being more responsive to changes in labor supply (Verme and Schuettler, 2021; Dustmann et al., 2017), effects on participation are only slightly more negative for women and not significantly different. A priori, one could also expect labor market effects to be more severe for younger natives, since migrants are younger on average. However, as shown by Lebow (2022), migrants work in occupations that tend to employ older natives. Thus, it is not surprising that negative wage effects are slightly stronger for older natives, although, again, the differences are insignificant. 21 This is done by averaging the outcome within metro–year–group cells. The first stage F-statistic changes as the populationbased cell weights change. Observations remain clustered at the metro level because treatment is assigned at this unit. Table 1 Labor market effects of immigration (1) (2) (3) OLS 2SLS Test (1)=(2) (p-value) ln(hourly wage) −0.73* −1.05*** 0.209 (0.42) (0.22) ln(hours/week) 0.08 0.27 0.399 (0.26) (0.27) Unemployment 0.01 −0.08 0.255 (0.13) (0.07) Labor force participation −0.10 −0.21* 0.355 (0.12) (0.11) K-P Wald stat 23.35 N474 474 Year FE, City FE X X Notes: Outcomes are residualized and multiplied by 100. Observations are weighted by city– year population. Column 3 presents a Hausman test for endogenous regressors with robust standard errors. Cluster-robust standard errors are in parentheses.2SLS, two-stage least squares; FE, fixed effect; K-P Wald stat., Kleibergen-Paap Wald statistic; OLS, ordinary least squares. *p<0.10, **p<0.05, ***p<0.01.
Page 16 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 The results also show that the decrease in labor force participation is concentrated among workers younger than 25years of age, with a magnitude of −0.54pp from a 1pp increase in the migrant share, likely reflecting lower labor force attachment for these workers. In Table A11, I show that this is partially driven by reduced school dropouts. Among workers younger than 25years of age, there is a 0.39pp increase in the share of migrants who are not working and are attending school, and a net 0.2pp increase in school attendance relative to a mean of 54.6. However, these are only significant at the 10% level, and the results are not robust to dropping the metro areas located closest to the Venezuelan border, which are in the right tail of the migrant share distribution. I further discuss the importance of this robustness check in Section 8. I expect the wage effect to be larger for less-educated workers given the concentration of migrants in low-skill occupations, and the results confirm this. The hourly wage effect, respectively, for those with less-than-secondary, secondary, and postsecondary education is −1.42%, −0.86%, and −0.75%. This pattern of negative wage effects decreasing in the education of natives is also observed when the sample is split by occupation groups, defined by ranking occupations Table 2 2SLS estimates by demographic groups (1) (2) (3) (4) (5) ln(hourly wage) ln(hours/week) Unemployment LFP K-P Wald stat. All −1.05*** 0.27 −0.08 −0.21* 23.35 (0.22) (0.27) (0.07) (0.11) Male −1.16*** 0.37** −0.05 −0.18** 24.34 (0.22) (0.17) (0.08) (0.08) Female −0.91*** 0.19 −0.12 −0.22* 22.22 (0.25) (0.39) (0.08) (0.13) Age 15–24years −0.94*** 0.14 −0.01 −0.54*** 21.34 (0.20) (0.46) (0.12) (0.18) Age 25–34years −0.97*** 0.31 −0.13 −0.08 22.11 (0.22) (0.21) (0.10) (0.07) Age 35–44years −1.10*** 0.29 −0.06 −0.07 23.39 (0.23) (0.20) (0.07) (0.06) Age 45–54years −1.01*** 0.34 −0.10** −0.11 26.11 (0.26) (0.25) (0.05) (0.10) Age 55–64years −1.21*** 0.24 −0.02 −0.10 23.71 (0.30) (0.38) (0.05) (0.11) Less than secondary −1.42*** 0.50 −0.05 −0.23* 28.72 (0.23) (0.34) (0.06) (0.12) Secondary −0.86*** 0.32 −0.02 −0.12** 25.64 (0.22) (0.21) (0.09) (0.06) Postsecondary −0.75* −0.02 −0.18* −0.24 17.22 (0.38) (0.23) (0.10) (0.16) Notes: Outcomes are residualized and multiplied by 100. All models include Year FE and City FE. Observations are weighted by city–year–group population. Cluster-robust standard errors are in parentheses.FE, fixed effect; K-P Wald stat., Kleibergen-Paap Wald statistic; LFP, labor force participation. *p<0.10, **p<0.05, ***p<0.01.
Page 17 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 according to mean preperiod native years of schooling and split into deciles. This is shown in Figure 3, where the coefficient hovers around −1.5 in the lowest three deciles, around −1 in Deciles 4 and 5, and between −0.5 and 0.0 for the top five deciles.22 I also split outcomes for workers by the “type” of work, grouped into four mutually exclusive categories: formal salaried, informal salaried, own account, and employer (representing 29%, 20%, 47%, and 4% of native workers, respectively). Self-employed workers may experience different effects of competition with migrants considering that they compete directly over prices rather than wages. Self-employed workers who hire employees, on the other hand, may experience increases in profits if the price of labor decreases. I split salaried workers according to formality status because we expect informal workers to face more direct competition with migrants and to have more flexible wages.23 Figure A5 shows that the wage effects are driven by informal salaried and own-account workers. Formal salaried workers also experience a wage decrease, but the coefficient is 50% smaller and not statistically different from zero. As I show in Section 9.2, this may be partly explained by the small exit out of formal work, which could mitigate the estimated wage effects for formal workers. The sample of employers is too small to generate precise estimates about the effects of migration on their profits. 7 Reconciling Results in the Literature 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 22 Estimates within occupation groups may be biased if workers switch occupations in response to the migration. In Section 9.2, I show that there are very small effects on movements across these groups. 23 More than 90% of own-account workers are informal, so I do not split that group into formal and informal. Figure 3 The effect of migration on residual ln(hourly wage) is separately estimated via 2SLS within occupation skill groups. Note: 95% confidence intervals are presented around each point estimate.
Page 18 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 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 1pp 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 highwage 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.24,25 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.26 The wage effects based on the 1993 and 2005 census IVs are similar in magnitude, driven by the high correlation in the migrant shares across these years. The IV based on distance to the border also produces similar results, though the magnitudes tend to be slightly larger. That these IVs generate similar results is not surprising given that border proximity is correlated with historical migrant shares. However, one may be concerned that border proximity is less likely to satisfy the exclusion restriction than historical migrant shares. These historical shares were small, determined decades earlier, and induced little immigration before 2015, while border proximity has the potential to be directly affected by economic changes related to the crisis. In Section 8, I treat border proximity as an omitted variable, correlated with historical migrant shares and potentially with trends in the outcome, rather than as a source of exogenous variation. I will show that controlling for a time trend interacted with border proximity somewhat reduces the magnitude of the wage effect. 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 24 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. 25 In an alternate approach, Penaloza-Pacheco (2021) estimates the average effect for the border departments La Guajira and Norte de Santander using a group of hand-selected departments as a control group or a synthetic control method. These methods estimate total wage effects of −13% and −9.4%, respectively, or −1.03% and −0.75% from a 1pp increase in the migrant share. These are more consistent with my own estimates, though they should be interpreted as the average effect specifically for these two departments. 26 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.
Page 19 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 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.27 The geographic level of analysis is, therefore, not a factor that drives large differences across papers, though when the department level is combined with the distance IV, the coefficient becomes notably larger (−1.27 relative to –1.05 using the 2005 census IV at the CZ metro level, which I refer to, going forward, as the “baseline specification”).28 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, Venezuelanborn 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 27 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. 28 The remaining paper that estimates a smaller wage elasticity of around −0.5 is by Bonilla-Mejía et al. (2020), using the 2005 census IV at the administrative metro area level. This result can be explained by the fact that they use total wages, not hourly wages, as the outcome. While this generates an effect size of −0.78 in that baseline specification (as can be seen in Table 1), it falls to −0.5 using the administrative metro areas. As we have seen, part of the effect on native total income is mitigated by an increase in hours worked.
Page 20 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 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 2018.29Particularly, the specification is ,2014 2018 ,2018c cc YM − ∆ =+ β (6) 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.30 A final paper is by Caruso et al. (2021), which finds a negative wage effect of −7.6% from a 1pp 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 1year, rather than 5years. 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 29 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. 30 Another result unique to Delgado-Prieto (2021) is the large estimated negative employment effect of −1.7% from a 1pp 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.
Page 21 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 using a migration flow rather than a migration stock on the right-hand side.31 In the two-way fixed effect framework, the resulting coefficient thus measures the effect of a change in the flow of migrants who arrived over the previous year. For example, in Bogotá, the 5-year migrant share was 0.48% in 2016 and 1.05% in 2017. Likewise, the 1-year migrant share was 0.24% in 2016 and 0.56% in 2017, the latter approximately reflecting the change in the 5-year migrant share over this period. When the model compares the change in the 1-year share, it attributes changes in the average wage in Bogotá between 2016 and 2017 to a change in migration of 0.32pp, rather than the 0.57pp increase in the migrant stock that actually occurred. In doing so, the researcher implicitly assumes that the economic effects of migration do not persist for >1year. 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 −3.53.32 Using the distance IV at the department level, the coefficient increases further to −4.17. When data are restricted to 2017, the coefficient inflates even further, to −4.80 in the baseline specification and −6.33 using the distance IV at the department level. Thus, the magnitude found by Caruso et al. (2021) can be explained primarily by the use of flows rather than stocks, second by the termination of analysis in 2017, and third by conducting analysis at the department level combined with an instrument based on distance to the border.33 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. 8 Additional Robustness 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. 31 According to the GEIH, only 0.23% of the population had come from Venezuela in the past 5years in 2014. Thus, using the 5-year migration measure until 2019 essentially measures the stock of migrants in the country who arrived since 2014. 32 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. 33 Indeed, in Table A4 in the Online Appendix, Caruso et al. (2021) run a specification in which they replace the 1-year migration measure with a 5-year migration measure, and the results are comparable with what I find here. However, these are not the primary results reported in the Abstract and Introduction sections.
Page 22 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 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 100km 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 >100km 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.34 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.35 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 −0.70.36 34 Trade data were downloaded from DANE and measure the net weight of all Venezuelan imports and exports with origin or destination in each department. 35 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. 36 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.
Page 23 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 Table 3 2SLS estimates’ robustness (1) (2) (3) (4) (5) (6) Original 2SLS Drop <100km from border Control trade with Venezuela Year trend× inverse distance to border Year trend ×region Year trend× pre-trend ln(hourly wage) All −1.05*** −1.02 −1.07*** −0.53 −0.59** −1.06*** (0.22) (0.68) (0.21) (0.67) (0.28) (0.22) Less than secondary −1.42*** −1.43** −1.45*** −0.45 −0.57 −1.42*** (0.23) (0.64) (0.22) (0.57) (0.40) (0.23) Secondary −0.86*** −0.93 −0.86*** −0.54 −0.32 −0.87*** (0.22) (0.68) (0.22) (0.58) (0.23) (0.22) Postsecondary −0.75* −0.65 −0.76** −0.33 −0.71** −0.82** (0.38) (0.99) (0.35) (1.18) (0.30) (0.36) ln(hours/week) All 0.27 −0.50* 0.27 −0.68*** 0.47* 0.28 (0.27) (0.28) (0.28) (0.24) (0.24) (0.26) Less than secondary 0.50 −0.58 0.51 −0.74** 0.67** 0.52 (0.34) (0.37) (0.35) (0.31) (0.30) (0.34) Secondary 0.32 −0.29 0.32 −0.37 0.50** 0.32* (0.21) (0.28) (0.21) (0.25) (0.23) (0.17) Postsecondary −0.02 −0.52* −0.04 −0.80*** 0.16 −0.02 (0.23) (0.28) (0.25) (0.22) (0.22) (0.22) Unemployment All −0.08 −0.15 −0.09 −0.38** −0.25* −0.12 (0.07) (0.20) (0.07) (0.16) (0.13) (0.08) Less than secondary −0.05 −0.13 −0.06 −0.34** −0.17* −0.07 (0.06) (0.17) (0.06) (0.13) (0.10) (0.07) Secondary −0.02 −0.21 −0.02 −0.41*** −0.21 −0.04 (0.09) (0.19) (0.08) (0.16) (0.14) (0.08) Postsecondary −0.18* −0.21 −0.18** −0.47** −0.37** −0.19* (0.10) (0.24) (0.09) (0.24) (0.18) (0.10) LFP All −0.21* 0.07 −0.20* 0.05 −0.20** -0.13 (0.11) (0.18) (0.11) (0.23) (0.09) (0.09) Less than secondary −0.23* 0.09 −0.23* 0.04 −0.20* −0.17 (0.12) (0.23) (0.12) (0.31) (0.11) (0.11) Secondary −0.12** −0.02 −0.09 0.00 −0.14*** −0.11 (0.06) (0.15) (0.07) (0.17) (0.05) (0.07) Postsecondary −0.24 0.13 −0.25 0.17 −0.26** −0.21 (0.16) (0.16) (0.16) (0.19) (0.13) (0.15) K-P Wald stat. 23.35 13.07 28.14 13.95 88.40 23.61 Number of metro areas 79 73 79 79 79 79 Notes: Outcomes are residualized and multiplied by 100. All models include Year FE and City FE. See text for description of robustness checks. Observations are weighted by city–year–group population. Cluster-robust standard errors are in parentheses.FE, fixed effect; K-P Wald stat., Kleibergen-Paap Wald statistic; LFP, labor force participation. *p<0.10, **p<0.05, ***p<0.01.
Page 24 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 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.37 Next, I drop all metro areas with an annual sample size of <1,000 observations, resulting in 27 major cities closely overlapping with the 23 official areas for which the GEIH is representative. This is to ensure that measurement error within small areas is not driving results. Third, I show that a first-difference model, in which the change in the outcome between 2014 and 2019 is regressed on the change in the migrant share, instrumented with the change in the instrument, produces results very similar to the two-way fixed-effects framework. This ensures that the bias of using two-way fixed effects in a context with potentially dynamic treatment effects is small, which was expected in this case, considering that most migrants did not arrive until close to the end of the study period. Fourth, there is a concern that the metro population, which is correlated over time, is in the denominator of both the endogenous variable and the instrument, and this may induce a spurious correlation that drives the first stage (Clemens and Hunt, 2019; Kronmal, 1993).38 To test this, I replace the Venezuelan share of the population, Mct, with a variable that represents the total number of Venezuelans. I then flexibly control for the baseline population by interacting it with year fixed effects. The results, in Column 10, show that the first stage remains strong, and that an increase of 100 migrants significantly reduces wages by 0.66%. At the mean population of 18,756, a 1% increase in the migrant share is therefore associated with a −1.23% wage effect, closely matching the initial estimates. Similar results are seen for other outcomes and subgroups. The final robustness check, regarding native internal migration, is discussed in Section 9.3. 9 Additional Results 9.1 Nonlinear effects The analysis thus far assumes a log-linear relationship between wages and migration. To allow for nonlinearity in the migrant share, in Table A7, I run a quadratic model in which I include the squared migrant share as an endogenous variable and the squared instrument as an additional instrument. Overall and within education groups, the curvature is positive, but it is insignificant and extremely small in magnitude. With every 1pp increase in the migrant share, the wage effect diminishes by 0.02 off a base effect of −1.5. 37 I can also drop all metro areas one by one, and this is available upon request. 38 For example, as discussed by Clemens and Hunt (2019), citing Kronmal (1993), “One would find storks-per-woman to be a strong instrument for babies-per-woman even if storks are irrelevant to babies, and that framework could show spuriously that babies cause any regional outcome that is correlated with the number of women in the region.”
Page 31 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 fact that migrants compete more directly with natives in these sectors. Moreover, as hypothesized, the wage effect becomes less negative as the ease of starting a business increases, though this is only significant at the 10% level. For departments 1SD above and below the mean score in ease of starting a business, the wage effect is −0.99 and −1.57, respectively. None of the other Doing Business indicators are significant. Table A10 shows that the result of wage effects increasing in informality and decreasing in ease of doing business are robust to the same list of robustness checks previously considered, though, in some cases, the standard error increases and the first-stage F-statistic becomes weak. The informality interaction coefficient becomes even larger and more significant with the inclusion of region-specific time trends, while the ease of doing business interaction coefficient remains stable. Overall, the results are suggestive that the ease of doing business and the size of the informal sector are relevant contributors to the wage effects of migration. From a policy perspective, this may indicate that it is desirable to not only reduce formality and facilitate business formation but also encourage or subsidize migrant relocation to areas that are better prepared according to these characteristics [as discussed regarding the Colombian setting, for example, in Bahar et al. (2018)]. 10 Conclusion 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 25years 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-edu- cated 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 1pp increase in the migrant share. First, when the
Page 32 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 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. Declarations Availability of data and material The data for this paper was provided by the Departamento Administrativo Nacional de Estadística (DANE) in Colombia and it is not publicly available at the level of geography that I use. While I therefore cannot provide the micro-data used in analysis, I can provide the Stata code and guidance for how to request this data directly from DANE. Competing interests The author, Jeremy Lebow, declares that he has no relevant or material financial interests that relate to the research described in this paper. Funding No additional funding, beyond the author’s PhD stipend, was received for this research. Author’s contributions This is a solo-authored paper, and it was completed entirely by the author without any other contributors. Acknowledgment I thank Duncan Thomas, Daniel Xu, Arnaud Maurel, and Erica Field, along with two anonymous referees and participants at the Duke Labor and Development workshops, for all of their helpful comments. I am also grateful to the Departamento Administrativo Nacional de Estadística (DANE) in Colombia for generously providing the data used in this paper. References Agudelo, Sonia A.; Hector Sala (2017): Wage Rigidities in Colombia: Measurement, Causes, and Policy Implications. Journal of Policy Modeling 39(3), 547-567. Akgündüz, Yusuf Emre; Huzeyfe Torun (2018): Two and A Half Million Syrian Refugees, Skill Mix and Capital Intensity. Technical Report. GLO Discussion Paper No. 186. Aksu, Ege; Refik Erzan; Murat Güray Kırdar (2018): The Impact of Mass Migration of Syrians on the Turkish Labor Market. Technical Report. Working Paper No. 1815. Alix-Garcia, Jennifer; David Saah (2010): The Effect of Refugee Inflows on Host Communities: Evidence from Tanzania. The World Bank Economic Review 24(1), 148-170. Alix-Garcia, Jennifer; Sarah Walker; Anne Bartlett; Harun Onder; Apurva Sanghi (2018): Do Refugee Camps Help or Hurt Hosts? The Case of Kakuma, Kenya. Journal of Development Economics 130, 66-83. Altındağ, Onur; Ozan Bakiş; Sandra. Rozo (2020): Blessing or Burden? Impacts of Refugees on Businesses and the Informal Economy. Journal of Development Economics 146, 102490. Altonji, Joseph G.; David Card (1991): The Effects of Immigration on the Labor Market Outcomes of Less- Skilled Natives, John M. Abowd and Richard B. Freeman, editors, in: Immigration, Trade, and the Labor Market. Chicago: University of Chicago Press, 201-234.
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Page 36 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 Appendix Table A1 Characteristics of migrants and nonmigrants Nonmigrants Migrants Male (%) 48.5 49.6 (50) (50) Age (years) 36.5 31.5 (13.9) (11.3) Labor force participation (%) 71.7 79.4 (45) (40.5) Unemployment (%) 11.4 14.8 (31.7) (35.5) Median hourly wage (2010 USD) 2.3 1.6 (6.1) (4.8) Hours/week 45.2 49.6 (15.9) (17.4) Own account (%) 25.3 32.1 (43.5) (46.7) Informal (%) 56 88.3 (49.6) (32.1) N447,264 21,730 Notes: Means are presented, SDs are in parentheses; data are restricted to urban residents of age 15–64 years. Migrant is defined as anyone in 2019 who was living in Venezuela 5years ago. Population weights are applied. GEIH, Colombian National Integrated Household Survey; SD, standard deviation. Source: GEIH (2019). Table A2 Preperiod correlates of 2005 Venezuelan share of population (1) (2) (3) (4) (5) Population (100,000) −0.001 0.005 0.004 0.004 0.002 (0.005) (0.003) (0.003) (0.003) (0.003) 100*ln(hourly wage) −0.017** −0.018* −0.018* −0.024* (0.008) (0.009) (0.009) (0.026) 100*ln(hours/week) 0.021 0.021 0.026 (0.017) (0.017) (0.019) 100* unemployment rate 0.047 0.049 (0.125) (0.126) 100* LPP rate 0.041 (0.047) N79 79 79 79 79 R21.6e−04 0.051 0.073 0.073 0.09 2014 metro characteristic Mc,2005 Mc,2005 Mc,2005 Mc,2005 Mc,2005 Notes: Mc,2005 is the 2005 Venezuelan share of the metro area, which ranges from 0% to 0.9%, and has been normalized to a mean of zero and SD of one. Observations are weighted by 2014 population. Robust standard errors are in parentheses. LPP, Labor force participation; SD, standard deviation. *p<0.10, **p<0.05, ***p<0.01.
Page 37 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 Table A3 Wage estimate sensitivity Panel A: including return migrants (1) (2) (3) (4) OLS IV: 2005 census IV: 1993 census IV: inverse distance Geographic unit: CZ metro areas Migrant share −0.73* −1.05*** −1.13*** −1.16*** (0.42) (0.22) (0.21) (0.17) K-P Wald stat. 23.35 21.78 28.54 Number of units 79 79 79 79 Geographic unit: administrative metro areas Migrant share −0.67 −0.94*** −1.03*** −1.08*** (0.49) (0.26) (0.20) (0.16) K-P Wald stat. 29.58 19.88 46.11 Number of units 23 23 23 23 Geographic unit: department Migrant share −0.83 −1.19*** −1.21*** −1.27*** (0.51) (0.28) (0.30) (0.18) K-P Wald stat. 19.07 20.90 35.20 Number of units 24 24 24 24 Panel B: excluding return migrants (5) (6) (7) (8) OLS IV: 2005 census IV: 1993 census IV: inverse distance Geographic unit: CZ metro areas Migrant share −0.87** −1.24*** −1.32*** −1.34*** (0.42) (0.26) (0.25) (0.21) K-P Wald stat. 26.42 21.52 29.50 Number of units 79 79 79 79 Geographic unit: administrative metro areas Migrant share −0.79 −1.09*** −1.18*** −1.24*** (0.48) (0.30) (0.23) (0.18) K-P Wald stat. 30.17 17.76 39.35 Number of units 23 23 23 23 Geographic unit: department Migrant share −0.97* −1.41*** −1.44*** −1.48*** (0.52) (0.34) (0.35) (0.21) K-P Wald stat. 19.55 19.38 31.37 Number of units 24 24 24 24 Notes: The outcome, namely, log hourly wage, is residualized and multiplied by 100. All models include Year FE and Unit FE. Panel A includes Colombian-born migrants in the migrant share, while Panel B excludes them. Columns 2–4 use different share components of the shift-share IV, based respectively on the complete 2005 census (as in the main analysis), the 10% subsample of the 1993 census, and the inverse minimum driving distance from the metro area or department capital to the closest Venezuelan border crossing. Geographic units include the 79 CZ-defined metro areas (as in the main analysis), the 23 official metro areas of which the GEIH is representative, and the 24 departments of Colombia. Observations are weighted by unit–year population. Cluster-robust standard errors are in parentheses. CZ, commuting zone; FE, fixed effect; GEIH, Colombian National Integrated Household Survey; IV, instrumental variable; K-P Wald stat., Kleibergen-Paap Wald statistic; OLS, ordinary least squares. *p<0.10, **p<0.05, ***p<0.01.
Page 38 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 Table A4 Wage estimate sensitivity: 2014–2018 difference model Panel A: including return migrants (1) (2) (3) (4) OLS IV: 2005 census IV: 1993 census IV: inverse distance Geographic unit: CZ metro areas Foreigner share (2018 GEIH) −0.26 −1.07*** −1.05*** −1.24*** (0.60) (0.39) (0.35) (0.24) Foreigner share (2018 census) −0.54 −1.26*** −1.21*** −1.45*** (0.49) (0.46) (0.42) (0.28) Number of units 79 79 79 79 Geographic unit: administrative metro areas Foreigner share (2018 GEIH) −0.09 −0.87** −0.89*** −1.07*** (0.63) (0.43) (0.33) (0.23) Foreigner share (2018 census) −0.39 −1.13** −1.09** −1.35*** (0.54) (0.57) (0.43) (0.29) Number of units 23 23 23 23 Geographic unit: department Foreigner share (2018 GEIH) −0.25 −1.02*** −0.97** −1.19*** (0.59) (0.39) (0.41) (0.23) Foreigner share (2018 census) −0.46 −1.36*** −1.32** −1.53*** (0.79) (0.50) (0.53) (0.29) Number of units 24 24 24 24 Panel B: excluding return migrants (5) (6) (7) (8) OLS IV: 2005 census IV: 1993 census IV: inverse distance Geographic unit: CZ metro areas Foreigner share (2018 GEIH) −0.62 −1.58*** −1.53*** −1.80*** (0.75) (0.58) (0.52) (0.34) Foreigner share (2018 census) −0.65 −1.55*** −1.46*** −1.77*** (0.55) (0.56) (0.51) (0.34) Number of units 79 79 79 79 Geographic unit: administrative metro areas Foreigner share (2018 GEIH) −0.36 −1.27** −1.26*** −1.54*** (0.76) (0.63) (0.48) (0.32) Foreigner share (2018 census) −0.48 −1.38** −1.31** −1.65*** (0.61) (0.70) (0.53) (0.36) Number of units 23 23 23 23 Geographic unit: department Foreigner share (2018 GEIH) −0.55 −1.54*** −1.43** −1.77*** (0.75) (0.59) (0.61) (0.33) Foreigner share (2018 census) −0.55 −1.81*** −1.72** −2.02*** (0.99) (0.67) (0.70) (0.38) Number of units 24 24 24 24 Notes: See notes to Table A3. This model is a regression of the change in residual wages from 2014 to 2018 on the 2018 foreigner share, calculated using the GEIH or Census as a share of the 2018 population. The instrument is created analogously (interacted with the national migration rate from the GEIH or census). In no case does the K-P Wald statistic fall below 10. CZ, commuting zone; FE, fixed effect; GEIH, Colombian National Integrated Household Survey; IV, instrumental variable; K-P Wald stat., Kleibergen-Paap Wald statistic; OLS, ordinary least squares. *p<0.10, **p<0.05, ***p<0.01.
Page 39 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 Table A5 Wage estimate sensitivity: 1-year migration measure Panel A: including return migrants (1) (2) (3) (4) OLS IV: 2005 census IV: 1993 census IV: inverse distance Geographic unit: CZ metro areas 1-year migrant share (data until 2019) −1.45 −3.53*** −3.96*** −3.82*** (1.29) (0.80) (0.90) (0.67) 1-year migrant share (data until 2017) −2.18 −4.80*** −5.15*** −5.74*** (2.35) (1.36) (1.25) (0.91) Number of units 79 79 79 79 Geographic unit: administrative metro areas 1-year migrant share (data until 2019) −1.38 −3.05*** −3.60*** −3.58*** (1.67) (0.89) (0.82) (0.59) 1-year migrant share (data until 2017) −2.76 −4.40** −5.03*** −5.65*** (3.03) (1.74) (1.35) (0.96) Number of units 23 23 23 23 Geographic unit: department 1-year migrant share (data until 2019) −1.80 −4.01*** −4.31*** −4.17*** (1.65) (1.01) (1.19) (0.63) 1-year migrant share (data until 2017) −3.58 −5.38*** −5.29*** −6.33*** (3.15) (1.59) (1.63) (0.92) Number of units 24 24 24 24 Panel B: excluding return migrants (5) (6) (7) (8) OLS IV: 2005 census IV: 1993 census IV: inverse distance Geographic unit: CZ metro areas 1-year migrant share (data until 2019) −1.74 −3.75*** −4.28*** −3.94*** (1.29) (0.85) (1.06) (0.75) 1-year migrant share (data until 2017) −3.64 −5.51*** −5.92*** −6.64*** (2.85) (1.48) (1.30) (0.96) Number of units 79 79 79 79 Geographic unit: administrative metro areas 1-year migrant share (data until 2019) −1.58 −3.03*** −3.55*** −3.55*** (1.57) (0.87) (0.79) (0.59) 1-year migrant share (data until 2017) −3.78 −4.85** −5.49*** −6.42*** (3.23) (1.88) (1.40) (1.02) Number of units 23 23 23 23 Geographic unit: department 1-year migrant share (data until 2019) −1.97 −4.14*** −4.45*** −4.30*** (1.63) (1.03) (1.21) (0.67) 1-year migrant share (data until 2017) −4.82 −6.68*** −6.50*** −8.07*** (3.41) (1.93) (1.93) (1.08) Number of units 24 24 24 24 Notes: See notes to Table A3. This is the original two-way fixed-effects model, replacing the 5-year migrant share with the 1-year migrant share (the share of the population that arrived from Venezuela in the past 12months) and varying the end of the period of analysis. In no case does the K-P Wald stat. fall below 10. CZ, commuting zone; FE, fixed effect; GEIH, Colombian National Integrated Household Survey; IV, instrumental variable; K-P Wald stat., Kleibergen-Paap Wald statistic; OLS, ordinary least squares. *p<0.10, **p<0.05, ***p<0.01.
Page 40 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 Table A6 2SLS estimates additional robustness (1) (2) (3) (4) (5) (6) Original 2SLS Drop Bogotá Drop metro yearly sample <1,000 2014–2019 Difference model Kronmal specification Assign natives to past metro ln(hourly wage) All −1.05*** −1.03*** −1.04*** −1.09*** −0.66*** −1.04*** (0.22) (0.22) (0.23) (0.27) (0.15) (0.20) Less than secondary −1.42*** −1.41*** −1.41*** −1.33*** −0.95*** −1.38*** (0.23) (0.24) (0.25) (0.27) (0.17) (0.22) Secondary −0.86*** −0.87*** −0.85*** −0.79*** −0.54*** −0.80*** (0.22) (0.22) (0.23) (0.28) (0.15) (0.21) Postsecondary −0.75* −0.69* −0.75* −0.96** −0.46** −0.80** (0.38) (0.37) (0.39) (0.48) (0.23) (0.36) ln(hours/week) All 0.27 0.28 0.27 0.27 0.17 0.29 (0.27) (0.27) (0.27) (0.32) (0.17) (0.27) Less than secondary 0.50 0.52 0.51 0.51 0.34 0.51 (0.34) (0.34) (0.34) (0.39) (0.22) (0.34) Secondary 0.32 0.32 0.30 0.26 0.20 0.32 (0.21) (0.21) (0.21) (0.26) (0.12) (0.21) Postsecondary −0.02 −0.02 −0.00 0.01 −0.01 0.02 (0.23) (0.22) (0.22) (0.25) (0.12) (0.22) Unemployment All −0.08 −0.08 −0.09 −0.07 −0.05 −0.07 (0.07) (0.07) (0.08) (0.07) (0.04) (0.07) Less than secondary −0.05 −0.05 −0.06 −0.03 −0.04 −0.06 (0.06) (0.07) (0.07) (0.06) (0.04) (0.06) Secondary −0.02 −0.01 −0.03 0.02 −0.01 −0.01 (0.09) (0.08) (0.09) (0.09) (0.05) (0.08) Postsecondary −0.18* −0.18* −0.17* −0.20* −0.11* −0.15 ( 0.10) ( 0.10) ( 0.10) ( 0.10) ( 0.06) ( 0.10) LFP All −0.21* −0.21** −0.21** −0.17* −0.13** −0.20** ( 0.11) ( 0.11) ( 0.10) ( 0.10) ( 0.07) ( 0.10) Less than secondary −0.23* −0.24* −0.24** −0.16 −0.16* −0.24** (0.12) (0.12) (0.11) (0.10) (0.08) (0.12) Secondary −0.12** −0.12** −0.12** −0.10 −0.07** −0.12** (0.06) (0.06) (0.06) (0.07) (0.04) (0.05) Postsecondary −0.24 −0.25 −0.23 −0.27 −0.15* −0.21 (0.16) (0.16) (0.17) (0.18) (0.08) (0.15) K-P Wald stat. 23.35 23.41 19.28 30.89 24.17 24.47 Number of metro areas 79 78 27 79 79 79 Notes: Outcomes are residualized and multiplied by 100. All models include Year FE and City FE. Column 4 regresses the change in outcomes from 2014 to 2019 on the change in the migrant share. Column 5 replaces the migrant share with the number of migrants (divided by 100) and controls for baseline population interacted with year FEs. Column 6 assigns natives to their 5-year lagged metro area of residence. Observations are weighted by city–year– group population. Cluster-robust standard errors are in parentheses. 2SLS, two-stage least squares; FE, fixed effect; K-P Wald stat., Kleibergen-Paap Wald statistic; LFP, labor force participation. *p<0.10, **p<0.05, ***p<0.01.
Page 47 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 Figure A2 Concentration of migrants and natives across occupations. Notes: Data restricted to urban residents of age 15–64 years. Occupations ranked according to mean years of completed schooling for natives in the GEIH between 2010 and 2015. GEIH, Colombian National Integrated Household Survey. Source: GEIH (2019). Figure A3 Relationship between 2019 and 2005 migrant shares. Note: RMSE, root mean square error.
Page 48 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 Figure A4 Pre-trends in labor market outcomes. Note: Pre-trends estimated according to Eq. (5) in Section 5. They are 95% confidence intervals.
Page 49 of 49 Lebow. IZA Journal of Development and Migration (2022) 13:05 Figure A5 2SLS coefficient plot – by work sector. Note: 2SLS, two-stage least squares. They are 95% confidence intervals. Figure A6 LOWESS plot. Note: LOWESS, locally weighted scatterplot smoothing. The red dotted line displays the least square line of best fit.