This article estimates the effect of crime on migration rates for counties in U.S. metropolitan areas and makes three contributions to the literature. First, I use administrative data on migration flows between counties, which gives me more precise estimates of population changes than data used in previous studies. Second, I am able to decompose net population changes into gross migration flows in order to identify how individuals respond to crime rate changes. Finally, I include county-level trends so that my identification comes from shocks away from the trend. I find effects that are one-fiftieth the size of the most prominent estimate in the literature; and although the long-run effects are somewhat larger, they are still only approximately one-twentieth as large. I also find that responses to crime rates differ by subgroups, and that increases in crime cause white households to leave the county, with effects almost 10 times as large as for black households.
During the late 1980s and early 1990s, crime rates in U.S. metropolitan areas rose dramatically, from an average of less than 67 crimes per 1,000 people to almost 75 crimes per 1,000—an increase of 12 %. At the same time, a number of different factors caused central cities to be depopulated, and some of this depopulation was likely in response to the deterioration of quality of life resulting from increases in crime.
Two articles have looked at the effect of crime on the population change in central cities, but both articles focused on net population changes (Cullen and Levitt 1999; Ellen and O’Regan 2010). Because crime is a locational disamenity, we would expect some individuals to respond to changes in it by relocating. In this article, rather than focusing on net population changes, I use data that allow me to decompose net changes into gross migration flows, which allows me to directly estimate where people are moving in response to crime.
The effect of crime on location decisions is important because it enables us to calculate the total cost of criminal activity. If individuals decide to relocate within the same metropolitan statistical area (MSA) in response to increases in crime in a county, the individual likely does not have to incur additional job search costs but may still incur additional commuting and housing search costs. However, if an individual moves outside an MSA entirely, he or she will incur job search and housing search costs. Some previous estimates of migration on crime, such as those of Cullen and Levitt (1999), have implied that the costs of crime are large. However, I find effects that are much smaller, which suggests that costs are more modest.
This article contributes to the literature in three main ways. First, using data on county-to-county migration flows from the Internal Revenue Service (IRS), I decompose net population changes into gross population flows into and out of a county, from within and outside the MSA. This decomposition allows me to identify more precisely the margin on which population is adjusting in response to shocks to the crime rate. Second, because the IRS migration data are administrative, my population measures are subject to considerably less measurement error than population estimates used in the aforementioned two articles. Finally, I include county-specific trends, allowing me to address potential omitted variables at the county level that change over time, which has some effect on the estimates.
I find that a 10 % increase in the crime rate causes net population to decrease by 0.02 %. Additionally, I find no effect of crime on within-MSA migration, but rather that increases in crime rates cause individuals to leave the MSA. I also estimate that the cumulative effect of crime rate changes after three years is almost four times larger than the initial effect. Finally, I find evidence of differences in response to crime by demographic subgroup. I document evidence of “white flight,” showing that an increase in crime rates is associated with a larger negative percentage change in the white population: my point estimates are 10 times as large for whites than for blacks.
My results are much smaller than previous estimates in the literature, sometimes as small as one-fiftieth the magnitude. The main reason for this difference is that the data I use to measure population changes have less measurement error; previous articles have used population data with measurement error, which induces division bias in their estimates.
Additionally, I use my estimates to infer roughly how much of the decline in migration rates can be explained by the coincident decline in crime rates. I find that the decrease in crime rates between 1990 and 2009 can explain about 10 % of the decrease in migration rates over the same period, with estimates ranging from 3 % to 29 % of the decrease.
The article that first addressed the relationship between crime and population movements was that of Cullen and Levitt (1999). They used crime rate data from the Federal Bureau of Investigation (FBI) Uniform Crime Reports (UCR), which reports Index Crimes at the agency level (defined later in the article). Their sample comprised central cities of MSAs with populations greater than 100,000 in 1970: these are the areas that experienced the largest increases in crime during their period.1 Additionally, much prior research on this “flight from blight” phenomenon—notably that of Mieszkowski and Mills (1993)—suggested that high crime impacted how cities developed and their potential for growth.
Cullen and Levitt’s (hereafter, CL) main specification regresses changes in population on changes in crime rates, controlling for age distribution and demographics when possible. They measured population change in three ways. First, they constructed a yearly panel of central cities, measuring population changes using the population estimates from the UCR. Second, they used only census years in order to have a more precise measure of population changes as well as the ability to control for more covariates, such as percentage black and the education distribution. This approach also allowed them to see the longer-run response to changes in crime rates because using decennial census years effectively gave them a 10-year difference estimator. Finally, using the 1980 census and the data from the 5 % Public Use Microdata Sample (PUMS), they estimated five-year differences between 1975 and 1980.
Their findings were consistent across approaches: a 10 % increase in crime causes a decrease in population of about 1 %, which they claimed implies that the migration response to crime occurs rather quickly. Additionally, by using migration data from the 1980 PUMS, they found that individuals who left central cities in response to higher crime rates were more likely to stay in the MSA than individuals who moved for other reasons.
There are a few concerns with the CL article. First, crime was secularly increasing during the sample period, while central city populations were in secular decline, which may have led to a spurious relationship. Second, CL’s claim that crime caused individuals to move only to the suburbs, but not to leave the MSA, was based on evidence from cross-sectional regressions, which suggests that omitted variables bias may be an issue.
Additionally, there are systematic errors in how the FBI calculates population for any geographic area smaller than a U.S. state, introducing measurement error into the population measure.2 CL’s main empirical specification of changes in population (in year t) on changes in crime (in year t) introduces the possibility of division bias, mechanically producing a more negative estimate.
Ellen and O’Regan (2010) (hereafter, EO) discussed this point in an article extending CL’s analysis through the year 2000. In their article, they showed that the CL estimates are sensitive to lagging the measure of change in crime and that the effect goes away when lagged (and actually becomes slightly positive). EO suggested that this implies that division bias drives the size of CL’s estimates and argued that lagging crime rates is more appropriate theoretically to estimate the effect of crime on population changes because it gives agents time to adjust their location decisions.
Additionally, by extending the analysis through 2000, EO addressed the first weakness of CL by including a period when crime was not secularly increasing. Overall, they found weak evidence that crime affects population changes.
Finally, they used the same approach as CL to identify where individuals moved in response to the changes in crime, using the 2000 5 % PUMS to identify individuals who moved within or out of the central city. They found evidence that individuals move from central cities to suburbs in response to increases in crime rates.
Both articles have similar shortcomings. The predominant limitation of these articles is the measurement error in the population from the FBI reports, which causes mechanical correlation between the main independent variable (crime rates) and the dependent variable (changes in population). Additionally, neither article was able to look at the direction of population flows in a panel setting: their results that individuals moved to suburbs in response to crime shocks came from cross-sectional regressions, which did not allow them to absorb important cross-city differences. Finally, they did not include city-specific linear time trends, which may absorb differences in how certain areas are changing over the period.
This article addresses each of these concerns. First, I use IRS Statistics of Income migration data to measure migration to and from a county. Because these data are administrative, they are less likely to be subject to measurement error.3 Second, because I am using county-to-county migration data, I can test more directly CL’s claim that increases in crime cause individuals to move to the suburbs. Although my data cannot identify within-county moves, if I find that the coefficient on the crime rate is significant when the dependent variable is within-MSA migration, that would confirm CL’s hypothesis. Additionally, I can test this hypothesis with a panel of counties, which allows me to control for county-specific unobservable factors. Finally, I include county-specific linear time trends, which impacts the estimates considerably.
In another important article related to this one, Gould et al. (2002) argued that local labor market conditions, particularly for lower-educated males, are a strong determinant to crime. This observation means that controlling for labor market conditions at the local level is important given that it is strongly correlated both with migration and with crime rates.
My sample includes all counties that are in an MSA according to the 1990 MSA definitions provided by the U.S. Census, with the data spanning the period 1980 to 2010, although the IRS migration data span only from 1984 to 2010. I also restrict the sample further to include MSAs with two or more counties.4 I implement the first restriction because an MSA is a natural definition of a local labor market, and so my measure of local labor demand (defined later in this section) functions well in this context. I implement the second restriction in order to consistently identify the two different margins of migration response: namely, within-MSA migration and outside-MSA migration.
The migration data I use in this article are from the IRS Statistics of Income files. In these data, the IRS reports two different measures of migration: the number of returns that move from one county to another, and the number of exemptions that move from one county to another. The first measure is a proxy for the number of households moving from county to county, and the second is a proxy for the number of individuals moving. Because I am interested in total population movements, I use the number of exemptions throughout this article. The migration data from the IRS are reported as migration from April of one year to April of the next year (e.g., April 1983 to April 1984); I assign the migration figures to the later year. These migration rates are comparable with measures of migration from other sources (Molloy et al. 2011: figure 2).
Using the migration data, I construct five outcome variables: net migration, out-migration to counties in the same MSA, out-migration to counties outside the MSA, in-migration from counties in the same MSA, and in-migration from counties outside the MSA. Following Saks and Wozniak (2011), all variables are measured as rates, where the denominator is the number of exemptions in the county in the previous year.5
Migration rates are expressed as migrants per 1,000 people. Table 1 shows that the average migration rate during the period of study is just under 61 people per 1,000; almost two-thirds of that migration is outside the MSA. In contrast, the net migration rate is particularly small, at only 1 person per 1,000. This illustrates my earlier point that simply looking at net changes obscures most of the population movements that are occurring. The time series of migration rates is shown in Fig. 1; the migration rate begins about 67 per 1,000 but falls by over 10 by 2009. Although the migration rate appears to fall significantly from 2007 to 2010, it is the result of the increase from 2005 to 2007; the decrease in migration to 2010 is pretty close to the general trend.
To estimate crime rates, I use the FBI UCR from 1980 to 2009. The UCR reports tally monthly counts of crimes at the police agency level, which I aggregate to the county-year level. These reports document only Index Crimes, which are considered the most serious offenses. These offenses are separated into violent crimes (murder, rape, robbery, and aggravated assault) and property crimes (burglary, larceny, arson, and auto theft). Additionally, if two crimes are reported in one incident, only the more serious crime is recorded. Agencies that are larger than a county are given different identifiers for each county in which they operate. The reports also include the population covered by the agency. I use this population measure as my denominator to calculate crime rates, following Cullen and Levitt (1999) and Ellen and O’Regan (2010). Each county has an average of seven agencies, with a median of four.6
Using UCRs is not devoid of problems, and others have discussed these issues at length.7 Because the FBI does not require individual agencies to report crime counts, some agencies in some years did not report any crimes. I address this issue by systematically dropping agencies that failed to report crimes in three consecutive years of the data. I detail my procedure for dropping these agencies in Appendix A. Because this procedure interpolates crime counts for some agencies, the measure of crime counts is subject to some measurement error.
Summary statistics for crime rates, presented in Table 1, are reported as incidents per 1,000 people. The average total crime rate for the period is around 60 crimes per 1,000 people, but crime rates are highly heterogeneous across counties. I report crime rates for each individual crime type as well as the crime categories. Violent crime is a much smaller proportion of the crime reported, and assaults make up a large share of violent crime. Additionally, larceny is a large portion of the property crimes.
Crime rates are in decline over much of my sample period, as Fig. 1 shows. Since the peak in 1990, crime has been steadily declining, falling by almost 30 % from 1990 to 2009. Additionally, Fig. 2 shows that both the levels and the variance of crime rates differ across MSAs. For example, Albany (New York) has relatively low crime rates, and the rates are steady throughout the sample period; by contrast, Atlanta (Georgia) has a large increase in crime until 1990, and then long-run declines since then. Los Angeles (California) is somewhere in the middle in both levels and variation.
where ηjk,1980 is the initial share of industry j in MSA k in 1980. The second term in parentheses is the national annual growth rate of hours worked in industry j, excluding MSA k. Summing over these yields Demandkt, which is the exogeneous shock to labor demand in year t for MSA k.
I strictly prefer my Bartik instrument to MSA unemployment rates for three reasons. First, because the MSA boundaries changed considerably over the period I study, the area over which the MSA unemployment rate was measured also changed. This may lead to changes in the unemployment rate even if there are no corresponding changes to labor demand in the MSA. By using the demand index, I fix the area over which labor demand is being measured, ensuring a consistent definition of the local labor market. Second, the unemployment rate is also a function of population changes because it is the equilibrium for the supply and demand of labor; however, the demand index as defined earlier does not have this property because it only identifies the changes to labor demand that are exogenous to the local market. Finally, substate estimates of the unemployment rate are known to have measurement error, which could lead to attenuation of the estimated coefficients. For all these reasons, I prefer the demand index to the unemployment rate to control for local labor market conditions.
Because the migration rate of individuals is also correlated with the demographics of the county, I use the 1980, 1990, 2000, and 2010 censuses to obtain county-level measures of the age distribution, percentage black, percentage with a bachelor’s degree or higher, and median household income expressed in 2010 dollars. To fill the gaps between censuses, I use the Survey of Epidemiology and End Results (SEER) population estimates to calculate the age distribution and percentage black.8 Finally, because there are no other sources for most of the years of my sample for percentage holding a BA and median family income, I interpolate those values for the intercensal years.
From a seminal study by Roback (1982) and a more recent article by Moretti (2011), we know that population flows are one way in which local economies attain spatial equilibrium in response to labor demand and amenity shocks. In the theory presented in both of these articles, a shock to an amenity or labor demand in year t should affect the location decisions of individuals in the following year. One such amenity that changes over time is the crime rate. Linden and Rockoff (2008) showed that crime is a salient disamenity for individuals, and for this reason, shocks to crime may cause individuals to relocate.
where yckt is the migration rate from or to county c of MSA k in year t; Demandk,t − 1 is the labor demand index for MSA k in year t – 1, calculated from Eq. (1); and CrimeRateck,t – 1 is the crime rate in county c and MSA k for year t − 1. Xck,t − 1 are county-level demographic controls; and δt and λc are year and county fixed effects. Finally, ηc × t are county-specific linear time trends. Standard errors are clustered at the MSA level to address correlation in labor demand and crime over time within an MSA. Additionally, I weight all regressions by lagged county population.
Equation (2) is similar to CL’s and EO’s estimating equations but with a few important differences. First, instead of using MSA unemployment rates as the measure of labor demand, I use a Bartik demand index because it directly measures the exogenous changes to labor demand. Additionally, rather than using contemporaneous changes in crime as the outcome variable, I use the lagged level of crime rates; given that migration decisions take time to execute, we should expect that lagging crime rates is a more accurate approximation of the truth.
Previous studies in this literature made some attempt to instrument for crime. The authors sought to solve two problems by instrumenting for crime: (1) division bias resulting from measurement error in the population, and (2) the endogeneity of crime rates with respect to population changes.
As discussed earlier, I address the first problem of measurement error in the population by using the IRS data, which are administrative, to measure the change in population and gross migration flows. Finally, because the measurement error in the UCR population is likely to be uncorrelated with any measurement error in the IRS data, they will not induce the division bias present in previous studies.
To address the problem of endogeneity, which is the second concern requiring instruments, I changed the estimating equation in two important ways. In my estimating equation, I used lagged crime rates so that the crime rates are realized before individuals decide to move, eliminating a mechanical correlation between the two variables.9 Given that individuals consider shocks that occurred in the previous period as well as some expectation over the future level of crime rates when deciding their location decisions, this lagged crime rate is more theoretically appropriate.
Additionally, to further address the potential endogeneity of crime, I control for county-specific trends.10 Given that my identification of β in Eq. (2) leverages time-series variation in crime rates, I want to ensure that my results are not based on long-run trends in crime, but rather that I am identifying the migration response resulting from shocks to crime rates that deviate from the long-run trend (that an individual could have predicted).
To the extent that those changes do not completely solve the issue of endogeneity, it is important to think about how this would bias my estimate of the effect of crime on migration. Thus, I present two ways that crime might be endogenous and consider how my estimate would be affected.
First, if individuals had plans to migrate and therefore reduced their investment in their community (thereby reducing the social capital in the area), that may increase the crime rate; and if they then migrate after crime has increased (even though they planned to move before the increased crime), this would positively bias the effect of crime on outmigration. One way to test this story is to include an additional lag of crime rates; little change in the main estimate would suggest that my estimate does not suffer from large bias.
Second, suppose that migration rates are high in an area and that they are increasing. Under this scenario, migration rates in the present would be correlated with past migration rates, and past migration rates would mechanically increase crime rates (assuming that the number of crimes does not change) because the denominator is shrinking. This would also positively bias my estimate of crime on outmigration; however, this story will likely be addressed by the inclusion of county-level trends.
Most other scenarios also suggest a positive bias in my estimate. However, given that I show in my Results section that the estimate I find is much smaller than previous estimates in the literature, I am not concerned that this bias is driving my findings.
Finally, the previous articles in this literature have demonstrated that finding an appropriate instrument in this setting is difficult. Both CL and EO instrument for crime using prison admission and release flows at the state-level as a proxy for the severity of the state criminal justice system; however, the statistics they reported call into question the validity of these instruments. CL’s instrument never had an F statistic above 6.5; EO’s fails the test of overidentifying restrictions. Additionally, the article underlying their instrument—Johnson and Raphael (2012)—showed that the relationship between prison flows and crime rates was much weaker after 1991, which is most of the period I study. Finally, in the literature on the causes of crime, notably Gould et al. (2002), the only variable strongly correlated with crime rates is the labor demand for high school dropouts, but that variable is not excludable because it also affects migration rates.
To first show estimates comparable to those of the previous literature, I estimate the effect of lagged crime rates on net migration rates. The results are shown in Table 2. Net migration is calculated as in-migration minus out-migration, so that a negative coefficient implies that an increase in crime causes more people to leave than to enter the county. Column 1 includes year and county fixed effects, column 2 adds controls for the age distribution of a county, and column 3 controls for other demographics. Column 4 includes county trends, and column 5 includes a control for the crime rate in the rest of the MSA. Finally, column 6 restricts the analysis to 1984–1993 to see whether the effect is larger in that period (the second half of the period CL studied).
My preferred estimate is in column 4. To compare this estimate with the previous literature, I must estimate what effect a 10 % increase in crime has. In my sample, a 10 % increase in crime is 5.85, and so the coefficient in column 4 implies that a 10 % increase in crime leads to a decrease in the net migration rate of 0.239, almost 50 times smaller than the CL estimate of a 1 % decrease in population. In fact, when I restrict my analysis to the period CL studied, I find a similar sized effect (smaller but not statistically different).
One important difference between the CL specification and my own is the unit of observation and the sample restrictions. CL looked at central cities, whereas I look at all counties in an MSA. Additionally, CL restricted their sample to central cities with populations of more than 100,000 people in 1970. Finally, the CL sample spans 1975 to 1993, and my sample spans 1984 to 2010. To see whether these differences in my specification or sample are driving the smaller results, I reestimate Eq. (2) in Appendix B with various restrictions. Although I find a slightly larger effect, it is still almost 30 times smaller than CL estimates.
One other potential explanation for the differences between my results and CL is that my data do not measure within-county moves, which were about 62 % of all migration in 2006–2010. Given that the boundaries of a central city overlap with county boundaries in many cases, individuals could leave the central city and still stay in the same county.
I cannot measure within-county moves, but suppose that the data existed; I can calculate how large the intracounty response would have to be for CL’s finding to be accurate. Their finding is that a 10 % increase in crime causes a 1 % decrease in population. For their estimate to be true, the intracounty migration rate would have to increase by 9.746 (because the intercounty migration rate increased by 0.239). Given that a 10 % increase in crime is 5.85, the coefficient in this theoretical regression would have to be 1.67, which is two orders of magnitude larger than my coefficient on net migration, which seems much larger than is plausible.11
Although my estimates are much smaller than CL’s, they are much closer in magnitude to those of EO, who found very small effects of crime on net population changes. Additionally, my estimate is closer to related estimates in the migration literature; Saks and Wozniak (2011) found that a 1 standard deviation increase in national labor demand increased migration rates by only 0.2 people per 1,000. Because the effect is small for a large shock to labor demand, it would be odd to expect a large effect for crime, which is just one amenity of many in a city.12
In addition to looking at the net migration effects of crime rates, my data enable me to decompose the net migration rate into its four components: out-migration to counties within the MSA, out-migration outside the MSA, in-migration from counties within the MSA, and in-migration from outside the MSA. This allows me to directly test how individuals respond to a shock in the crime rate, using the same identification strategy as I do for net migration rates.
My results estimating each of these four components as a dependent variable are presented in Table 3. In each panel, column 1 includes county and year fixed effects, column 2 includes controls for the age distribution, and column 3 includes controls for other demographics. My preferred estimate is column 4, which includes county-specific trends. To ensure that my results are not sensitive to its inclusion, in column 5, I include a control for crime rates in the rest of the MSA.
My estimates for outmigration within the MSA are mostly positive, although generally small and insignificant, implying that crime increases do not cause much relocation within an MSA. By contrast, increases in crime cause a significant increase in out-migration to counties outside the MSA. In my preferred specification (column 4), it is the only significant result. Additionally, there is suggestive evidence that in-migration rates from outside the MSA decrease in response to higher crime rates, suggesting that individuals that would have moved to a county are less likely to do so if crime increases. To see that the decomposition worked properly, notice that all the coefficients on crime in column 4 of Table 3 add up to the estimate on crime in Table 2, column 4.13
Although my findings seem at odds with the prior literature’s conclusion that individuals relocate within the MSA, two main explanations show this difference. First, CL and EO use cross-sectional variation for identification, which makes them unable to control for differences across cities and time. By using a panel of counties in MSAs, as well as data on migration flows rather than merely population changes, I can properly identify the migration response. Second, as mentioned earlier, my data do not measure within-county moves; thus, I cannot definitively state that individuals are not moving within the MSA, although I can assert that individuals do also leave the metropolitan area in response to crime rates.
The point estimates of the demand coefficients in Table 3 are also informative. When the dependent variable is within-MSA migration, the coefficients are uniformly insignificant, which makes sense given that the demand index is measured at the MSA level. However, increases in local labor demand cause fewer individuals to leave the MSA: the coefficient is significantly negative when the dependent variable is out-migration outside the MSA, a result that is robust to the inclusion of county trends.
Longer-Run Responses to Crime Changes
Using this formula, a two-year difference of out-migration to outside the MSA would be the sum of the number of out-migrants in years t and t + 1, divided by the population in year t. This exercise allows me to trace long-run response of migration to crime.14
I show my results for out-migration to outside the MSA and in-migration from outside the MSA in Table 4. Below the standard errors of the coefficients for crime rates, I also scale the point estimates in terms of a 10 % increase to the crime rate, for comparison to CL’s results. I find that the cumulative response of out-migration to outside the MSA after four years is almost five times the size of the initial response, implying that it takes considerable time for individuals to relocate. The estimate on the in-migration rate also suggests that individuals take time to adjust their information about a location: an increase in crime in year t has a larger total impact on migration rates over four years than after the initial year. However, my estimate is still much smaller than CL’s estimate.
Additionally, Table 4 suggests that labor demand shocks do not have long-run impacts on migration; after the first year, they are very noisy and uninformative, suggesting most of the response occurs in the first year. Overall, the long-difference results suggest that a crime change has longer-run impacts on migration.
To test the sensitivity of my estimation, I also perform a number of robustness checks. These results are presented in Tables 5 and 6, which test the sensitivity of my results to restrictions of the sample and the addition of other control variables, respectively. Starting with Table 5, column 1 shows my preferred specification (from column 4 of Table 3).
Column 2 of Table 5 restricts the analysis only to those counties with similar populations according to the UCR and the SEER population data. I find a larger effect, but the estimate is not significantly different from my main specification. In columns 3 and 4 of Table 5, I restrict the analysis to counties in MSAs that had populations larger than 100,000 and 500,000 in 1980, respectively. The results are consistent with my main specification.
I also want to investigate whether my finding of no effect on migration within an MSA due to crime rates is because there is less opportunity to undertake intercounty within-MSA migration when there are only a few counties. To test this hypothesis, in Table 5, columns 5–7, I restrict the sample to metropolitan areas with more than four, six, or eight counties. Although the coefficient on crime for out-migration within the MSA is larger in columns 5 and 6, the size of the coefficient is still only one-half as large as the main estimate for out-migration to outside the MSA. Therefore, my finding is not just a feature of there not being limited options to undertake an intercounty, within-MSA move. In fact, my coefficient for out-migration to outside the MSA (panel B) is increasing and significant, and is slightly larger than my main estimate.
Table 6 presents more checks, where I control for various other covariates that may affect both the migration rate and the crime rate; I present results here only for out-migration outside the MSA; other outcome variables are available upon request. Column 1 is my preferred estimate from Table 3, column 4. Column 2 controls for the poverty rate, which increases the coefficient on crime rate slightly, but it is not distinct from my original estimate.
Column 3 includes a measure of the racial fractionalization in an MSA, measured in a way similar to Alesina and La Ferrara (2000).15 When I include this measure, the coefficient becomes noisier and less significant but is not significantly different. One reason why it becomes noisier is that this measure is available only from 1986 onward (when the CPS identifies most MSAs), and so I lose a number of observations. Column 4 includes an additional lag of crime rates, and my coefficient does not change significantly, although it gets slightly smaller. Additionally, the second lag on crime is also statistically significant: the cumulative effect of crime rate shocks grows with time. Finally, column 5 includes all counties that are in metropolitan areas, rather than those in MSAs that have more than one county. The coefficient remains unchanged. Finally, in columns 6 and 7, I estimate Eq. (2) for different periods. My results suggest that most of the effect is from the first half of the period, which makes sense, given the higher crime rates during that era.
In results not shown, I also test whether my result is sensitive to how I restrict my sample. In my main analysis, some counties had quite unreliable crime data. To test whether my results are sensitive to the agency dropping procedure described in Appendix A, I ran my main specification including all the crime data. The coefficient on the crime rate is smaller and a bit more noisy, which is expected when measurement error is present as in the crime data. Overall, my main estimate is not sensitive to changes in specification and retains its statistical significance, which is particularly encouraging for my analysis.
Demographic Differences in Migration Response
One limitation of the IRS data is that they do not include any information on the demographics of the individuals moving. However, given that I have found a migration response to crime, I can use yearly percentage changes in population groups to see whether certain groups are moving in response to crime. I construct population counts from the SEER database for whites and blacks, and for the following age categories: 0–18, 19–44, 45–59, and 60 and older. I then construct the yearly percentage change in each population group and regress it as the dependent variable of Eq. (2).
My results are presented in Table 7. Although the coefficients are very small, I find suggestive evidence that younger people (ages 19–44) as well as whites are moving. This finding of “white flight” accords with the other literature on the subject. Interestingly, the coefficient on black percentage change in population is an order of magnitude smaller than the white response and is statistically insignificant. This result lines up with recent work by Sharkey (2013), who showed that black households have much lower migration rates in the most recent era and documented some of the consequences of these lower rates.
In this article, I make three important contributions to the literature on crime and migration. First, I decompose net migration flows into gross flows into and out of a county, within and outside an MSA. This decomposition allows me to show that increases in crime cause individuals to relocate outside the MSA but that there is no measurable effect on within-MSA migration. Second, I show that these results are robust to the inclusion of county-level trends. Finally, by using the IRS migration data rather than the population data in the UCRs, I address the issue of the measurement error in the population, which EO mentioned as one of the main confounders in estimating migration responses to crime rates. Taken together, my results show that the migration response to crime is much smaller than previously estimated.
Additionally, I show that increases in crime rates cause larger negative percentage changes for white populations and for young individuals, suggesting that they are leaving the county in response to crime. However, I find very small point estimates for blacks, which implies that they are very unresponsive to crime rates.
Using my results, I can also use my estimates to calculate roughly how much the decrease in crime, shown in Fig. 1, contributed to the decrease in the migration rate. Crime rates fell in my sample from a peak of 74.05 crimes per 1,000 people in 1989 to 47.43 per 1,000 in 2007, and further fell to 44.50 crimes per 1,000 people in 2009. Over the same period, migration rates fell from 62.95 to 58.37 per 1,000 from 1989 to 2007, and finally to 51.85 people per 1,000 in 2009. The coefficient on crime rates from my main specification is 0.0251, and the percentage of total migration that is out-migration to outside the MSA is 60.82 %. Using these figures, the decline in crime rates explains between 3.7 % to 9.8 % of the decline in migration rates over the same period. Additionally, using the coefficient from my long-run responses, 0.626, I can explain an average of 29 % of the decline in migration, depending on the ending year. This is relatively substantial and is about the same magnitude as the combination of the rise in homeownership and the aging of the U.S. population, which together explain 25 % of the decline in migration rates over this period, as calculated by Molloy et al. (2013).
I thank Ann Stevens and Giovanni Peri for their helpful feedback on all the drafts of this article, as well as participants in the UC Davis Public/Labor Graduate Student Brown Bag series and the Western Economic Association International conference session. I also thank Ingrid Gould Ellen for her helpful correspondence on an earlier version of this article. Finally, I thank the anonymous referees for their helpful comments, which helped to sharpen and clarify this article.
Appendix A: Uniform Crime Reports Data Elimination Procedure
Because of the inconsistency of reporting for some reporting agencies (hereafter, ORIs), I had to eliminate some ORIs and sometimes eliminate an entire county from the sample. The process for eliminating these ORIs is described in this appendix section. First, I assign each ORI a start year, when it first entered the data set; and an end year, the last year it reported crime data. Between these years, some 2004 ORIs never reported crime statistics; I omit these ORIs. If between the start and end years, the ORI is missing more than three years in a row or is missing more than half of its data (if it has four years), then that ORI is marked as “missing” and is eventually dropped. Overall, 1,600 ORIs are marked as missing. If fewer than three years in a row are missing, I interpolate the crime counts for each individual crime.
If the largest or second largest agency in a county (defined by the maximum yearly crime count) is marked as missing, I drop the county entirely. This occurs for 78 and 42 ORIs respectively, leading to a total of 78 of 754 counties being dropped from my sample. If the agency that is missing in a county is not the largest or second largest, which is the most common case, then I drop the ORI for the whole sample but not the county, which accounts for the remaining dropped ORIs, totaling 1,412. The median population coverage of the ORIs dropped from my analysis is 3,676; the median population coverage of ORIs included in my analysis is 6,960. This procedure leaves me with a sample of 4,901 ORIs in 676 counties. Most of the ORIs dropped are small.
I test whether nonreporting is correlated with any of my explanatory variables at the agency or county level, finding only slight indications that the number of crimes is negatively correlated with being a nonreporting agency. Thus, smaller agencies are a large share of nonreporting agencies, indicating that nonreporting will not significantly affect my county-level crime rates.
Appendix B: Comparisons With Cullen and Levitt (CL)
My main results differ from those of CL, and one concern is that my sample is more broad than theirs. To explore how these effects differ by sample selection, I estimate Eq. (2) on a number of subsamples, which are displayed in Table 8.
CL’s main sample includes “127 U.S. [central] cities with populations greater than 100,000 in 1970” (Cullen and Levitt 1999:160) for the years 1975–1993. My sample includes all counties in all metropolitan areas with more than two counties from 1984–2010. To closely proxy their sample, I include in column 1 only counties that are part of the central city of an MSA that is in the top 25 % of the population at the beginning of my sample, for the years 1983–1995, and weights by lagged county population. Then, in column 2, I include all MSAs. In column 3, I include all the years of my sample, still restricting the sample to include only central-city counties. Column 4 includes my estimates for all counties. Finally, column 5 shows my preferred specification, which includes county-specific linear trends. Although the coefficient is somewhat larger in column 1, the estimates do not change much across columns, suggesting that sample selection is not driving the differences between my results and CL’s.
The census defines central cities as “one or more of the largest population and employment centers of a metropolitan area.”
To calculate populations for areas at the substate level, the FBI uses decennial census data and the state population growth rate to determine the population in a city or county jurisdiction, which ignores any possible reallocation within the state. For more detail and explanation, see the Methodology section on the FBI UCR webpage (http://www.fbi.gov/about-us/cjis/ucr/frequently-asked-questions/ucr_faqs/%23methodology).
Importantly, any measurement error in the data is unlikely to be correlated with the measurement error in the FBI UCR population estimates and therefore will not introduce division bias.
This limits my sample from 205 to 105 MSAs. In results not shown, I find that my estimates do not change if I include all MSAs.
This means that the total outmigration rate in year t would be outmigrantst × 1,000 / (outmigrantst + nonmigrantst).
For example, Washtenaw County, Michigan (home of Ann Arbor, MI) has 14 agencies, which include the Washtenaw County Sheriff, Ann Arbor Police Department, Eastern Michigan University Police, and University of Michigan Police, among others.
The age distribution is measured in bins, ages 0–17, 18–24, 25–44, and 45–64. The omitted category is those 65 and older.
In the CL article, using contemporaneous changes in crime, if population fell for a reason not correlated with crime, that would have the effect of making net population change more negative while increasing crime rates mechanically (because the denominator is larger), making crime rates endogenous in the estimating equation.
My results are also robust to quadratic trends, but that is not my preferred specification.
In results not shown, I also calculated within-county migration using the CPS for the sample of counties that are identified. The coefficient on crime was insignificant and noisy.
Additionally, given the number of studies estimating how much central city depopulation is driven by various factors (Baum-Snow 2007; Boustan 2010; Margo 1992), it seems that we may be overexplaining central city depopulation. I am grateful to an anonymous referee for bringing this point to my attention.
In order to add them properly,
An alternative approach would be to include multiple lags of crime, which produces qualitatively similar results. The long-difference approach adopted here is more congruent with CL’s long-difference estimates.
The fractionalization measure is F = 1 − ∑isi2, where si is the share of the population for race/ethnicity i in an MSA; race/ethnicity is white, black, American Indian, Asian/Pacific Islander, or Hispanic. This measure is created in the spirit of a Herfindahl index.