The Labor Market Effects of Credit Market Information

The Labor Market Effects of Credit Market Information Abstract We exploit a natural experiment to provide one of the first measurements of the causal effect of negative credit information on employment and earnings. We estimate that one additional year of negative credit information reduces employment by 3 percentage points and wage earnings by $${\$}$$1,000. In comparison, the decrease in credit is only one-fourth as large. Negative credit information also causes an increase in self-employment and a decrease in mobility. Further evidence suggests this cost of default is inefficiently borne by those most creditworthy among previous defaulters. Received April 5, 2017; editorial decision September 2, 2017 by Editor Andrew Karolyi. Authors have furnished an Internet Appendix, which is available on the Oxford University Press Web Site next to the link to the final published paper online. Credit registries are an important tool used by lenders worldwide to obtain better information about borrowers and to strengthen repayment incentives. Several studies have documented that credit information affects borrowers’ access to credit.1 However, much less is known about the effects of credit information on noncredit outcomes such as employment that are critical for welfare and policy analysis. Credit information may affect employment indirectly through its effects on credit supply, but more direct channels are also possible. Indeed, while credit registries were largely established to improve the efficiency of credit markets, over time, noncredit actors have increasingly sought out their information (e.g., insurance companies, utilities, landlords, and mobile phone providers). Ample anecdotal (and some survey) evidence shows that many employers around the world also query credit registries when making hiring decisions.2 In this paper we provide one of the first measurements of the causal effect of negative credit information on employment and earnings. To do this, we obtain detailed tax, employment, and demographic records merged with data from the Swedish credit registry for a sample of people drawn from the universe of pawn-loan borrowers in Sweden. This sample is well suited to measure the employment effects of credit information because it is formed by people who are exposed both to financial distress and to frequent spells of unemployment. As a result, people in our sample are more weakly attached to the labor market and are likely to bear any employment cost of negative credit information, should this cost exist. In Sweden, like in most countries (e.g., Miller (2000)), information on the past repayment of debts and other obligations is collected and disseminated through credit registries, and mostly used by lenders to evaluate new borrowers. A borrower who defaults in Sweden receives an arrear in her file, and a nonpayment flag appears prominently on the top of the credit report.3 Swedish law mandates that each arrear must be deleted from an individual’s credit record 3 years after it was registered. In turn, the nonpayment flag at the top of the report remains until all arrears have expired. Our objective is to measure the causal effect on employment of having a past arrear reported in the credit record. However, a simple comparison of people with and without reported past arrears is likely to provide biased estimates of the causal effect of interest, as people with past arrears are more likely to be unemployed, independent of the nature of their credit information. To identify the causal effect, we exploit a policy change that varied the amount of time that arrears were reported by the credit registry in Sweden. Before October 2003, arrears were deleted on the last calendar day (i.e., December 31) of the third year after first being recorded. Beginning in October 2003, the law was reinterpreted and arrears were deleted exactly 3 years to the day after they were registered. We refer to the 2001 cohort of defaulters in our sample as the New regime and the 2000 cohort of defaulters as the Old regime. The policy change caused a decrease in the average retention time of past defaults for members of the New regime relative to the Old regime. Importantly, given that the policy change was announced in March 2003, all people who defaulted in 2000 or in 2001 did so under the same beliefs about the retention time of their flags of past defaults. Importantly for identification, the key impetus for this change was technological and coincided with an upgrade of the computer systems used by the registry. This policy change was first exploited by Bos and Nakamura (2014). We use the variation in the retention of past arrears induced by the policy change to identify the causal effect of negative credit information on employment outcomes. However, a simple comparison of people in the New and in the Old regime before and after the removal of their respective nonpayment flags would confound any causal effect of credit information with other annual trends in the Swedish economy. Instead, we take advantage of the fact that the policy change modified the retention time of the indicator of past defaults differentially for people who defaulted in different calendar months across the year. In particular, among people who received an arrear early in the year, those in the Old regime had a longer retention time than those in the New regime. In contrast, people in the New and Old regimes with an arrear late in the year faced the same retention time. Thus, in our main empirical strategy we compare the yearly employment outcomes of people in the New and Old regimes who received a nonpayment flag early in the year with those who received one late in the year and track how these outcomes change after the nonpayment flag is deleted. We find that the deletion of past defaults has large effects on employment. An individual in the New regime who defaulted early in the calendar year is approximately 3 percentage points more likely to be employed the year in which her nonpayment information is removed from the credit registry, relative to an individual in the Old regime and relative to an individual who defaulted late in the year. This difference persists (at least) 1 year after the information is deleted, albeit with a smaller magnitude. People whose information is removed earlier also earn higher wages and incomes, are less likely to pursue additional years of education, and are more likely to change residence. Moreover, people most exposed to the policy are less likely to be self-employed, suggesting that for our population of alternative borrowers, entrepreneurship acts more as a response to involuntary unemployment and less as a high-growth business opportunity. We estimate that removing an individual’s past nonpayment flag 1 year earlier raises yearly wages by approximately $${\$}$$1,000, an effect that is four times larger than the increase in consumer credit. Credit information may affect employment through two channels. First, as discussed above, employers may use credit information directly to screen employees.4 Second, improved credit information increases an individual’s access to credit, which may in turn impact employment in many ways. For example, more credit may allow people to make investments necessary for finding or keeping a job.5 Increased credit may also allow people to invest in entrepreneurship, thus reducing the relative value of wage labor.6 Further, if people use labor hours to smooth negative shocks in a precautionary manner, they may reduce their labor supply following an increase in access to credit.7 Distinguishing between these two mechanisms is important insofar as the policy responses that emerge from each are very different. Our baseline results rule out effects predominantly arising from the entrepreneurship and labor smoothing channels, by which more access to credit would lead to more wage employment.8 We exploit rich household-level data to provide two additional tests that suggest that employer screening is the main driver of our results. First, we study intra-household effects of nonpayment flag removal. If credit constraints impede a household’s labor supply, then we should expect employment effects on both the individual whose information is deleted and the spouse’s. However, we find no detectable treatment effect on the income of the spouse. Second, we explore differences in the information available to financial institutions versus employers. Crucially, employers are only able to observe a strict subset of the lender’s information. In particular, lenders can observe the number of arrears, while employers can only observe the presence of at least one arrear. We find that access to credit increases upon removal of the nonpayment flag but only for people who have many (above median) arrears removed from their record together with the nonpayment flag. There is no increase in credit upon removal of the nonpayment flag for people with few arrears. In contrast, we find that the effect of the removal of the past default flag on employment is positive, similar in magnitude, and statistically indistinguishable for people with many or few arrears.9 With the caveat that the sources of heterogeneity are not randomly determined and could thus reflect unobserved differences in labor market opportunities across groups, we view these results as broadly inconsistent with a model in which employment is mainly determined by differences in access to credit. This latter result also suggests a potential inefficiency in the use of credit market information by employers. Indeed, one possible interpretation of this result is that banks use all of the available information in their underwriting policies and recognize that borrowers with few arrears are more creditworthy. However, employers are forced to pool people with few or many arrears, leading to a uniform increase in employment post-deletion. Unless the information contained in past repayment behavior that is relevant for banks is not relevant for employment, such pooling disadvantages people with fewer initial arrears and also likely disadvantages firms.10 In summary, our contribution is threefold. First, we document and measure a large employment cost of default associated with credit information among people at the margins of formality. Second, our results suggest that this employment cost of default is largely driven by employer screening. Third, we show suggestive evidence that this employment cost of default is inefficiently borne by creditworthy people. Our paper contributes to a recent academic literature that provides mixed evidence of the employment effect of credit information. Cohen-Cole, Herkenhoff, and Phillips (2016b) document an increased flow into and out of self-employment after removal of the bankruptcy flag from credit records in the United States, while Dobbie et al. (2016) estimate that the removal of bankruptcy flags has no effect on employment. There are two key reasons why our results could differ from Dobbie et al. (2016). First, we focus on different types of credit information. While past defaults, which are our focus, can only be observed through credit reports, bankruptcies remain in the public record and can potentially be accessed by employers or job search agencies even when they have been deleted from credit records. Second, the timing of the credit information differs between the two papers. Past defaults in our setting are at most 3 years old, while bankruptcy flags are removed 7 or 10 years after filing. One interpretation of these different results is that the informational content of a bankruptcy flag received 7–10 years ago is relatively less important for employers than an individual’s more recent delinquencies. Finally, Balance, Clifford, and Shoag (2016), Bartik and Nelson (2016), and Cortes, Glover, and Tasci (2016) study equilibrium effects in the labor markets of bans imposed by U.S. states on the use of credit information on hiring decisions. Our work also speaks to several strands of household finance research. First, we contribute to the literature on the impacts of credit market information on credit market outcomes.11 Second, we add to previous work that studies the effects of debt renegotiation on households.12 Third, our paper is relevant for the literature on the interaction between entrepreneurship and credit supply (e.g., see the citations in footnote 6). Our findings also speak to the current academic and policy debates surrounding the appropriate scope of use for credit information by employers, in particular in the context of the increasing use of large data sets in economic decisions, that is, “big data” (e.g., see Einav and Levin 2014).13 1. Measuring the Employment Cost of Default 1.1 Setting and policy change 1.1.1 Swedish credit registries and policy change Credit registries are repositories of information on the past repayment of debts and other claims, such as utility bills, credit cards, and mortgage payments. In Sweden, credit registries collect registered data from 3 main sources: the national enforcement agency (Kronofogden), the tax authorities, and the Swedish banking sector.14 Each reported default triggers an arrear on the borrower’s credit report. In Sweden, any person or company can in principle buy and view the credit records of any other individual.15 Financial institutions that report to the registry are able to view the entire credit file, including the summary credit score and number of arrears, while noncontributing institutions and private people are only shown a strict subset of the recorded information. Noncontributing entities observe neither the credit score nor the number of arrears. They instead see a nonpayment flag, which indicates at least one arrear. Before October 2003, Swedish law mandated that all arrears be removed from each individual’s credit report 3 years after the nonpayment occurred. In practice, the credit registries removed all arrears on December 31 of the third year after the nonpayment occurred. Beginning in October 2003, the Swedish government changed the interpretation of the law to remove every past arrear from the credit registries exactly 3 years after the nonpayment was recorded.16 Notably for identification, the change was motivated by an upgrade to the registries’ IT capabilities and not by changes to the type or frequency of defaulters. As shown in Figure 1, the adjustment to the law induced a sharp change in the time series pattern of arrear removals by the credit registries. The figure plots the bimonthly number of people with arrears that were no longer reported in the credit registry. The figure shows that before 2003, arrears were almost only removed from the credit registry on the last day of the year.17 Further, the figure shows a noticeable spike in the frequency of removals in October 2003. This spike corresponds to the removal of the stock of arrears that had occurred between January and the end of September 2000 and that had not yet been deleted from the credit registry. After October 2003, the frequency is more smoothly distributed over the year, in effect following the distribution of nonpayments across the year, 3 years earlier. Figure 1 View largeDownload slide Frequency of removal of nonpayment flag over time This figure displays the distribution of the removal of nonpayments over time. In the Old regime the credit registry removed all eligible arrears once a year, on December 31. Because of the bimonthly feature of our data, and because removals are inferred as differences in the stock of reported defaults, these nonpayments corresponds to the February–March bimonth (labeled February). This regime ended at the end of September 2003, when the law change came into effect and the credit registry removed arrears exactly 3 years to the day after the default was first reported. Figure 1 View largeDownload slide Frequency of removal of nonpayment flag over time This figure displays the distribution of the removal of nonpayments over time. In the Old regime the credit registry removed all eligible arrears once a year, on December 31. Because of the bimonthly feature of our data, and because removals are inferred as differences in the stock of reported defaults, these nonpayments corresponds to the February–March bimonth (labeled February). This regime ended at the end of September 2003, when the law change came into effect and the credit registry removed arrears exactly 3 years to the day after the default was first reported. 1.1.2 Identification intuition We attempt to identify the causal effects of past nonpayment information on employment and other labor market outcomes. A simple correlation between credit information and employment would likely be plagued by both reverse causality and omitted variable bias.18 Rather, an idealized experiment to identify this causal effect would consider two identical groups of people who defaulted in the past and subsequently repaid but, as a result, have a bad credit record. In that experiment, the credit registry would delete the information for one group earlier than scheduled and any difference in the employment of both groups could be causally assigned to the removal of information. In our empirical setting, we use the variation in the retention time of publicly observable arrears induced by the 2003 policy change in Sweden to approximate this idealized setting. One naive empirical strategy would be to focus on nonpayment cohorts before the policy change and to compare people who defaulted earlier in the year to those who defaulted later in the year. After all, the early defaulters did experience longer retention times than the end-of-year defaulters. However, it is likely that people who default at different times during the year differ in ways that may have systematically different labor market outcomes.19 Further, people may have been aware of the pattern of deletions and chose to time their defaults accordingly if possible. Hence, a comparison of the employment prospects of people who defaulted early and late in the same year before the policy change is likely to be biased. An alternative identification strategy is to compare people who defaulted in 2000, which we define as the “Old regime,” with those who defaulted in 2001, which we define as the “New regime,” observing that the average retention time is lower for the New regime. Indeed, the policy change induced unexpected variation in the length of time that information was retained in the credit registries. Hence, people who defaulted in 2000, 3 years prior to the policy change, did so under the same beliefs about retention time as people who defaulted in 2001, 2 years before the policy change. The unexpected nature of the policy change allows us to rule out any strategic behavior of people timing their default so as to experience shorter retention times. However, this strategy is also problematic as there may be other differences between people who defaulted in 2000 or in 2001 that are correlated with labor market outcomes. Instead, we combine the two empirical strategies—New versus Old regime cohorts and early versus late defaulters within the calendar year—for identification. We compare the difference in the employment prospects of people in the New regime whose default was reported early and late in the year with the same difference for people in the Old regime. We observe that people in the New regime who defaulted at any point in 2001 and people in the Old regime who defaulted late in 2000 were subject to the same 3-year retention times. People in the Old regime group who defaulted early in 2000 were subject to more than 3 years of retention time. For example, people in the Old regime group who defaulted in March 1 were subject to 3 years and 7 months of retention time. This double-difference analysis is the basis of our identification strategy. We then compare the employment outcomes for each individual before and after the 3-year post-arrear date. The identification assumption we make is that, in the absence of the policy change, the difference in employment outcomes of people in the Old and New regimes whose defaults were reported early and late in the year would have remained constant before and after the deletion of the nonpayment flag. In Section 2.1 we provide pre-trends evidence that is consistent with this assumption. Finally, among people in the New regime, those who defaulted earlier in the year experienced a larger decrease in retention time than those who defaulted later in the year. This suggests an additional test of our identification strategy: the effects of the policy change should be monotonically decreasing in the time of the year during which defaults were initially reported. In Section 2 we provide evidence that is consistent with this intuition. 1.2 Data Our initial sample comprises the near universe of alternative credit borrowers in Sweden. This sample was generously supplied by the Swedish pawnbroker industry and contains registered information about the 332,351 people who took out at least one pawn loan between 1999 and 2012 (approximately 5% of the Swedish adult population). It is true that people who resort to pawn borrowing are systematically different from the Swedish population at large. Given that people typically turn to pawn loans when they are not able to access sufficient credit from formal sources to meet their demand, unsurprisingly, pawn borrowers tend to be poorer, are less likely to be employed, earn lower wages conditional on being employed, and are less likely to be homeowners (Bos, Carter, and Skiba 2012).20 To paint a more complete picture of the population of Swedish pawn borrowers, we plot for the years of our sample the age, education, income and credit score distribution, and compare it to the distributions of the Swedish population at large (see the Internet Appendix). From these plots we learn that, on average, the Swedish pawn borrower is younger, less educated, earns a lower income, and has a worse credit score (a higher probability of default) compared to the average Swede. Importantly, the policy we study only matters for the potential outcomes of people with arrears. So, it is useful to ask what fraction of total defaulters in Sweden is represented in our sample. While the average Swede has a 10% likelihood of having at least one arrear, the number is 46% in our sample. This implies that we have data on approximately one quarter of arrear-holders in the country. Given the poor financial records and weak attachment to the labor market of alternative borrowers, it is exactly this population that may experience the greatest benefits from a clean credit record. We obtain a bimonthly panel of credit data from the leading Swedish credit registry, Upplysningscentralen that ranges from 2000 to 2005. Each bimonthly observation contains a snapshot of the individual’s full credit report (i.e., amount of credit and repayment status on different obligations). Swedish credit registries also have access to data from the Swedish Tax authority and other agencies. This enables us to further observe variables such as home ownership, age, marital status, yearly income from work, and self-employment. Importantly, we observe when an individual’s nonpayment was first reported and subsequently removed by the credit registry. To measure labor market outcomes, we match the credit registry data with information obtained from Statistics Sweden (SCB). These data are at the yearly level from 2000 to 2005 and include information on each individual’s employment status. The data also include measures of individual income, wages, and income from self-employment plus total household disposable income. We defer an analysis of summary statistics of our main outcome variables until after we have presented our sample selection criteria. 1.3 Implementation of empirical strategy The key empirical goal of the paper is to understand what happens when the defaulter flag is removed exogenously from the top of the credit report. The natural experiment in the paper allows us a unique opportunity to use quasi-exogenous variation to measure this impact. However, as in any heterogeneous treatment effects setting, the experiment doesn’t impact all households equally. For example, households with no arrears (the always-takers) and households who continue receiving arrears even after the policy announcement (the never takers) should not be affected directly. Thus, we make a series of sample restrictions to attempt to isolate people who, ex ante, are most likely to be affected by the policy (the compliers). First, we include in our analysis sample only people who received an arrear for nonpayment in 2000 or in 2001 and thus had those nonpayment flags removed in 2003 or 2004. Second, we further restrict the sample to people who did not receive additional arrears in the subsequent 20 months (i.e., who repaid all their delinquencies) before the policy change. This restriction reduces the sample size by 67% (i.e., 33% of all people in our sample who had an arrear in 2000 or 2001 did not redefault in the next 20 months). The rationale for this 20-month window is as follows. Recall that our identification strategy requires categorizing people into New and Old cohorts. With a shorter than 20-month window, it becomes unclear whether an individual who recorded an arrear in March 2000 and another in October 2001 should be in the Old or New regime. It is also essential that our sample construction be predetermined relative to the policy change. Thus, a longer than 20-month window would be contaminated by the endogenous choice of redefault caused by the policy change.21 Third, because of the bimonthly nature of the credit registry data shared with the researchers (e.g., December–January defaulters are first reported in the February snapshot, February–March in the April snapshot, and so on), we restrict our sample to defaults occurring strictly after January 2000.22 For a similar reason we omit people whose defaults are removed from the credit registry in the December-January 2001 bimonth. Finally, we focus on people who are between 18 and 75 years old the year before information on past defaults is removed from the credit registry. These selection criteria, which are necessary to implement our empirical strategy, result in a sample of 15,232 people. Figure 2 depicts the time line of the policy change and how it affected the length of time in which nonpayments were reported for the people in our sample. In particular, nonpayments of people in the Old regime were recorded in the first months of the year were reported in the credit registries for a maximum of almost 3 years and 8 months until the end of September 2003, while nonpayments of people in the New regime were recorded in the first months of the year were reported in the credit registries for exactly 3 years. Figure 2 also shows the number of past defaulters in each of the bimonthly bins. Although there are substantially more early defaulters than late defaulters in both cohorts, these patterns are remarkably consistent across New and Old regimes. Figure 2 View largeDownload slide Time line This figure depicts the time line of the policy change that enforced a 3-year retention time for reporting defaults and how this policy generated variation in the retention time of the nonpayment flag. In particular, people whose nonpayment occurred early in 2001 had a reduced retention time of past nonpayments. In contrast, people whose nonpayment occurred early in 2000 were reported in the credit registries until October 2003. Figure 2 View largeDownload slide Time line This figure depicts the time line of the policy change that enforced a 3-year retention time for reporting defaults and how this policy generated variation in the retention time of the nonpayment flag. In particular, people whose nonpayment occurred early in 2001 had a reduced retention time of past nonpayments. In contrast, people whose nonpayment occurred early in 2000 were reported in the credit registries until October 2003. Table 1 reports the excess number of months above 3 years that the nonpayment flag of people in each of the four cells – New regime-Early, New regime-Late, Old regime-Early and Old regime-Late – is retained in the credit registry after the policy change. All people in the New regime have a retention time of 3 years (reported in the table as zero excess months above 3 years). Old regime people who defaulted early in the year have on average 6 extra months of retention time, calculated as follows: February defaulters have on average 7.5 extra months of retention time of their nonpayment flag – from any day in February to the first day of October – March defaulters have 6.5 extra months, April defaulters have 5.5 extra months, and May defaulters have 4.5 extra months. Assuming a uniform distribution of people across all 4 months results in an average extra retention time of 6 months. Finally, Old regime people who defaulted late in the year have 1 extra month of retention time (calculated as: August defaulters have 1.5 extra months, September defaulters have 0.5 extra months, and October and November defaulters have exactly 3 years of retention time given that the policy change occurred precisely on the first day of October). Table 1 Average retention months Early Late New regime 0 0 Old regime 6 0.5 Early Late New regime 0 0 Old regime 6 0.5 Average retention months of the nonpayment flag in the credit registry in excess of 3 years are shown for the New and Old regimes, who defaulted early (February–May) or late (August–November). Table 1 Average retention months Early Late New regime 0 0 Old regime 6 0.5 Early Late New regime 0 0 Old regime 6 0.5 Average retention months of the nonpayment flag in the credit registry in excess of 3 years are shown for the New and Old regimes, who defaulted early (February–May) or late (August–November). We define the indicator variable $$New_{i}$$ to equal one if borrower $$i$$’s last nonpayment occurred during 2001 and zero if it occurred during 2000. We interact $$New_{i}$$ with the dummy variable $$Early_{i}$$, which distinguishes between people whose nonpayments occurred early and late during the year. Because in our data each individual is assigned to a bimonthly cohort of defaulters, $$Early_{i}$$ equals one for people whose last nonpayment occurred in the February-March or April-May bimonths, and zero for people whose last nonpayment occurred in the August–September or October–November bimonths.23 Finally, we create a dummy, $$Post_{i,t}$$, which equals one for all event years after borrower $$i$$’s nonpayment signal is removed (2003 for the Old regime and 2004 for the New regime). The variable $$Post_{i,t}$$ is measured in event time $$t$$, which is normalized to zero in 2000 for the Old regime and in 2001 for the New regime. Thus, event time year 3 represents the year in which the nonpayment flag is deleted from the credit registry for any individual in our sample. Our main specification is the following reduced-form model: \begin{align} Employed_{i,t} & = \omega_{i}+\omega_{t}+\omega_{\tau}+\beta New_{i}\times Early_{i}\times Post_{i,t}+\delta Post_{i,t}\nonumber \\ & \quad + \gamma New_{i}\times Post_{i,t}+\lambda Early_{i}\times Post_{i,t}+\varepsilon_{i,t}.\label{eq:regression} \end{align} (1) We include individual fixed effects $$\omega_{i}$$, calendar year fixed effects $$\omega_{\tau}$$, and event time fixed effects $$\omega_{t}$$, as well as all double interactions that are not absorbed by fixed effects. For completeness, we present in the Internet Appendix selected Swedish macroeconomic indicators throughout our sample period.24 The table suggests that although there is some volatility in economic aggregates, no major recessions were observed in Sweden during this time period. In particular, gross domestic product (GDP) growth dropped from 4.7% in 2000 to 1.6% in 2001, although unemployment dropped from 5.8% to 5% in the same time frame. Inflation is relatively constant and below 2.41%, and unemployment varied between 5% and 8% throughout the sample period. The variable $$\omega_{i}$$ absorbs the baseline and interaction coefficients of $$New_{i}$$ and $$Early_{i}$$. The coefficient $$\beta$$, our key parameter of interest, measures the differential probability of being employed for the New and Old regimes, for people whose nonpayment was reported early in the year relative to those whose nonpayment was reported late in the year, the year(s) after each individual’s nonpayment is no longer reported relative to the 3 prior years. The coefficients $$\delta$$ and $$\lambda$$ capture differences in employment for people in the Old regime whose nonpayment occurred late and early in the year, respectively, the years after the arrear is deleted. Finally, $$\gamma$$ captures differential employment trends for all people in the New regime after their nonpayment information is no longer publicly available. 1.4 Summary statistics Before presenting the regression results, we present the definitions of our dependent variables in Table 2 and selected summary statistics in Table 3. We focus our analysis on employment outcomes, broadly construed. In addition to earnings and whether an individual has a job, we also consider alternatives to labor income, including seeking more education and turning to self-employment income. The top panel presents a brief definition for each of our outcome variables, and the lower panel displays selected sample statistics. Table 2 Definitions of dependent variables Employed A dummy that equals one if the individual is employed conditional on being in labor force 1(Wages$$>0$$) A dummy that equals one if the individual has positive income from work log(Income + 1) Logarithm of yearly post-tax income, in 100 SEK; zeros replaced by 1 log(Wages + 1) Logarithm of yearly pre-tax income from work, in 100 of SEK; zeros replaced by 1 Self-employed A dummy that equals one if the individual received positive wages from entrepreneurship Relocates A dummy that equals one if individual’s residence is in a different county from previous year Years of schooling Number of years of completed education, inferred from end of year level of education Financial inquiries Number of requests for an individuals’ credit report by financial institutions Nonfinancial inquiries Number of requests for an individuals’ credit report by nonfinancial institutions Employed A dummy that equals one if the individual is employed conditional on being in labor force 1(Wages$$>0$$) A dummy that equals one if the individual has positive income from work log(Income + 1) Logarithm of yearly post-tax income, in 100 SEK; zeros replaced by 1 log(Wages + 1) Logarithm of yearly pre-tax income from work, in 100 of SEK; zeros replaced by 1 Self-employed A dummy that equals one if the individual received positive wages from entrepreneurship Relocates A dummy that equals one if individual’s residence is in a different county from previous year Years of schooling Number of years of completed education, inferred from end of year level of education Financial inquiries Number of requests for an individuals’ credit report by financial institutions Nonfinancial inquiries Number of requests for an individuals’ credit report by nonfinancial institutions Table 2 Definitions of dependent variables Employed A dummy that equals one if the individual is employed conditional on being in labor force 1(Wages$$>0$$) A dummy that equals one if the individual has positive income from work log(Income + 1) Logarithm of yearly post-tax income, in 100 SEK; zeros replaced by 1 log(Wages + 1) Logarithm of yearly pre-tax income from work, in 100 of SEK; zeros replaced by 1 Self-employed A dummy that equals one if the individual received positive wages from entrepreneurship Relocates A dummy that equals one if individual’s residence is in a different county from previous year Years of schooling Number of years of completed education, inferred from end of year level of education Financial inquiries Number of requests for an individuals’ credit report by financial institutions Nonfinancial inquiries Number of requests for an individuals’ credit report by nonfinancial institutions Employed A dummy that equals one if the individual is employed conditional on being in labor force 1(Wages$$>0$$) A dummy that equals one if the individual has positive income from work log(Income + 1) Logarithm of yearly post-tax income, in 100 SEK; zeros replaced by 1 log(Wages + 1) Logarithm of yearly pre-tax income from work, in 100 of SEK; zeros replaced by 1 Self-employed A dummy that equals one if the individual received positive wages from entrepreneurship Relocates A dummy that equals one if individual’s residence is in a different county from previous year Years of schooling Number of years of completed education, inferred from end of year level of education Financial inquiries Number of requests for an individuals’ credit report by financial institutions Nonfinancial inquiries Number of requests for an individuals’ credit report by nonfinancial institutions Table 3 Summary statistics Mean SD Median Dependent variables (1) (2) (3) Employed 0.43 0.50 1(Wages$$> 0$$) 0.79 0.40 log(Income + 1) 5.62 2.91 7.03 Income 914 719 913 log(Wages + 1) 5.57 2.97 7.04 Wages 1,184 1,070 1,134 Self-employed 0.05 0.21 Relocates 0.07 0.27 Years of schooling 10.70 1.76 11 Financial inquiries 0.52 1.05 Nonfinancial inquiries 0.54 0.95 Age 42.83 13.00 42 Male 0.60 0.49 Home owner 0.09 0.29 Number of people 15,232 Mean SD Median Dependent variables (1) (2) (3) Employed 0.43 0.50 1(Wages$$> 0$$) 0.79 0.40 log(Income + 1) 5.62 2.91 7.03 Income 914 719 913 log(Wages + 1) 5.57 2.97 7.04 Wages 1,184 1,070 1,134 Self-employed 0.05 0.21 Relocates 0.07 0.27 Years of schooling 10.70 1.76 11 Financial inquiries 0.52 1.05 Nonfinancial inquiries 0.54 0.95 Age 42.83 13.00 42 Male 0.60 0.49 Home owner 0.09 0.29 Number of people 15,232 Panel A defines the dependent variables. Panel B presents sample statistics for the 3 years before flag deletion, including 2000, 2001, and 2002 for the New regime and 2001, 2002, and 2003 for the Old regime. Table 3 Summary statistics Mean SD Median Dependent variables (1) (2) (3) Employed 0.43 0.50 1(Wages$$> 0$$) 0.79 0.40 log(Income + 1) 5.62 2.91 7.03 Income 914 719 913 log(Wages + 1) 5.57 2.97 7.04 Wages 1,184 1,070 1,134 Self-employed 0.05 0.21 Relocates 0.07 0.27 Years of schooling 10.70 1.76 11 Financial inquiries 0.52 1.05 Nonfinancial inquiries 0.54 0.95 Age 42.83 13.00 42 Male 0.60 0.49 Home owner 0.09 0.29 Number of people 15,232 Mean SD Median Dependent variables (1) (2) (3) Employed 0.43 0.50 1(Wages$$> 0$$) 0.79 0.40 log(Income + 1) 5.62 2.91 7.03 Income 914 719 913 log(Wages + 1) 5.57 2.97 7.04 Wages 1,184 1,070 1,134 Self-employed 0.05 0.21 Relocates 0.07 0.27 Years of schooling 10.70 1.76 11 Financial inquiries 0.52 1.05 Nonfinancial inquiries 0.54 0.95 Age 42.83 13.00 42 Male 0.60 0.49 Home owner 0.09 0.29 Number of people 15,232 Panel A defines the dependent variables. Panel B presents sample statistics for the 3 years before flag deletion, including 2000, 2001, and 2002 for the New regime and 2001, 2002, and 2003 for the Old regime. Our summary stats are estimated on the 3 years before nonpayment flags are removed, which correspond to the years 2000, 2001, and 2002 for the Old regime and 2001, 2002, and 2003 for the New regime. Our main outcome variables are Employed, a dummy that equals one for people who were continuously employed throughout the year, and $$1\left(Wages>0\right)$$, a dummy that equals one if the individual received any wage income during the year. During those years, an average of 43% of people in our sample are employed during the full year, whereas 79% received some positive wage income. We view the discrepancy between both averages as consistent with two particular facts about our sample. First, people in our sample have much higher job instability than the average Swede, in part because of their lower levels of education. As a result, an individual in our sample is more likely to receive some positive income from wages and at the same time experience unemployment spells during the year, thus being categorized as not fully employed as per our main outcome variable. Second, because of their lower education, people in our sample are more likely to have temporary, low-skill employment contracts. We verify this notion using aggregate data from Statistics Sweden on the relationship between education levels and labor market contracts for the general Swedish population. We see that 14.1% of the employment of people who drop out of high school is temporary, while this figure drops to 10% for people with more than a high school eduation.25 Average after-tax income is equal to SEK91,400 (approximately $${\$}$$12,000). We use a log transformation of our income measures, which are in units of hundreds of Swedish Kronor (SEK), as the outcome variable in our regression tests, and average log(Income+1) is 5.6. Roughly 5% of all people in our sample are self-employed. Finally, people are 42.8 years old on average and 60% male. The low rates of formal employment and average wage earnings confirm that our sample is indeed situated at the margins of formality, where negative credit information could lead to costly labor market exclusion. For comparability, we present in in the Internet Appendix selected summary stats obtained from the credit registry for a random sample of the Swedish population and for a random sample of people with at least one arrear, both as of 2003. The average probability of having any wage income in our analysis sample is closer to the sample that represents all Swedish defaulters (79% in our sample versus 86% for the random sample conditional on default). Moreover, based on our calculations, the average income in our sample corresponds roughly to the 10th percentile of the income distribution in Sweden as of 2003, while the average income for the Swedish sample conditional on any arrear is at the 13th percentile that same year. One limitation of the data is that it does not include information on the individual’s job or industry. To provide additional context for our sample, we obtain from Statistics Sweden information on the most common jobs categorized by education levels during our sample period. For people with 9 to 12 years of education, common jobs include; caretaker in the health care sector, retail salesperson, finance and sales associate, truck driver, construction worker, and janitor.26 Several of these industries, such as financial services, transportation, retail, and construction, report to check credit records for their applicants.27 2. Results 2.1 Graphical evidence We start by showing graphically the event-time evolution of the average outcomes, which provides evidence in support of our identification assumption. The identification assumption for regression (1) is that, in the absence of the policy change, the probability of being employed for the New and Old regimes would have evolved in parallel between early and late in the year defaulters. We provide evidence that supports this assumption in Figure 3. The top panel shows the average of $$Employed$$ (we omit subindeces for brevity), defined as a dummy for whether the individual was fully employed throughout the entire year, as well as $$1(Wages>0)$$, the average of a dummy that equals one for people who receive any positive wage during the year. The x-axis shows event time years, which are defined starting at zero in 2000 for the Old regime and in 2001 for the New regime. We look for parallel trends in the preperiod, and indeed, there are no detectable differences in the trends of the difference of either variable between early and late defaulters in the New and Old regimes during the 3 years before removal of the nonpayment flag (i.e., in event times 0 to 2).28 Similar effects can be observed for the average log income and log wage income, where zeros have been replaced by ones, shown in the lower panel. These graphs provide evidence that is consistent with our identification assumption. Below we also provide a formal test of (absence of) pretrends using lagged outcomes in a regression setting. Figure 3 View largeDownload slide Pre-trends This figure shows that there is no difference in the preperiod trends (before the policy change) of the difference between Early and Late defaulters, in the New regime and in the Old regime for our main outcomes. The top panel shows preperiod trends for $$employed$$ and $$1(Wages>0)$$, which equals one if an individual received any wage income, and the lower panel shows the same for $$\log(Wages+1)$$ and $$\log(Income+1)$$, where zeros have been replaced by 1. The solid lines represent the differences in averages of the respective outcome variables between people who defaulted early in the year (high exposure) and people who defaulted late in the year (low exposure), for people in the Old regime. The dashed line represents the same difference for people in the New regime group. Figure 3 View largeDownload slide Pre-trends This figure shows that there is no difference in the preperiod trends (before the policy change) of the difference between Early and Late defaulters, in the New regime and in the Old regime for our main outcomes. The top panel shows preperiod trends for $$employed$$ and $$1(Wages>0)$$, which equals one if an individual received any wage income, and the lower panel shows the same for $$\log(Wages+1)$$ and $$\log(Income+1)$$, where zeros have been replaced by 1. The solid lines represent the differences in averages of the respective outcome variables between people who defaulted early in the year (high exposure) and people who defaulted late in the year (low exposure), for people in the Old regime. The dashed line represents the same difference for people in the New regime group. The figures also hint at our main results: people in the New regime who default early in the year exhibit a higher probability of employment and earn higher incomes after their nonpayment flags are removed relative to similar people in the Old regime. In general, the graphs show that the difference in employment outcomes between early and late defaulters is positive but decreasing over time for both cohorts, but, in event time 3, that difference shrinks less for New regime. This suggests that the effect is driven by a relatively lower probability of employment for people in the Old regime who default early in the year, which is consistent with the credit information mechanism. For these people, the past nonpayment flag remains in the credit records for an extra 6 months (above 3 years), relative to half an extra month of retention time for Old regime people who defaulted late and no extra months for people in the New regime, as is shown in Table 1. 2.2 Main results Table 4 presents the output of regression (1). Columns 1, 2, and 3 present the regression results when the outcome is Employed. Column 1 documents that the probability of employment for an individual whose information is reported for a shorter period increases by 2.8 percentage points the year the nonpayment is removed from the registry (year 3). This effect is a 6.5% increase relative to the preperiod average employment rate (43%).29 Column 2 shows that this effect is also significant for the combined 2 years after removal, although with a lower magnitude. Column 3 shows that focusing only on the second year after removal, the point estimate continues to be positive, although statistical significance is lost. Table 4 Employment outcomes Employed Employed Employed $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0280** 0.0203* 0.0125 0.0298** 0.0299*** 0.0295** (0.013) (0.012) (0.014) (0.012) (0.011) (0.014) Post-period (years) 1 2 Only 2 1 2 Only 2 Obs 50,623 63,113 50,482 50,623 63,113 50,482 $$R^{2}$$ 0.002 0.003 0.003 0.007 0.024 0.027 No. of people 12,664 12,664 12,664 12,664 12,664 12,664 Employed Employed Employed $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0280** 0.0203* 0.0125 0.0298** 0.0299*** 0.0295** (0.013) (0.012) (0.014) (0.012) (0.011) (0.014) Post-period (years) 1 2 Only 2 1 2 Only 2 Obs 50,623 63,113 50,482 50,623 63,113 50,482 $$R^{2}$$ 0.002 0.003 0.003 0.007 0.024 0.027 No. of people 12,664 12,664 12,664 12,664 12,664 12,664 This table shows that public information on past defaults causally reduces employment. The table shows the coefficient $$\beta$$ from regression: \begin{align*} Employed_{i,t}&= \alpha_{i}+\omega_{t}+\nu_\tau + \beta Early_i\times New_{i}\times Post_{i,t}+\delta Post_{i,t}\\ &\quad +\gamma New_{i}\times Post_{i,t}+\lambda Early_{i}\times Post_{i,t}+\varepsilon_{i,t}. \end{align*} Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 4 Employment outcomes Employed Employed Employed $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0280** 0.0203* 0.0125 0.0298** 0.0299*** 0.0295** (0.013) (0.012) (0.014) (0.012) (0.011) (0.014) Post-period (years) 1 2 Only 2 1 2 Only 2 Obs 50,623 63,113 50,482 50,623 63,113 50,482 $$R^{2}$$ 0.002 0.003 0.003 0.007 0.024 0.027 No. of people 12,664 12,664 12,664 12,664 12,664 12,664 Employed Employed Employed $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0280** 0.0203* 0.0125 0.0298** 0.0299*** 0.0295** (0.013) (0.012) (0.014) (0.012) (0.011) (0.014) Post-period (years) 1 2 Only 2 1 2 Only 2 Obs 50,623 63,113 50,482 50,623 63,113 50,482 $$R^{2}$$ 0.002 0.003 0.003 0.007 0.024 0.027 No. of people 12,664 12,664 12,664 12,664 12,664 12,664 This table shows that public information on past defaults causally reduces employment. The table shows the coefficient $$\beta$$ from regression: \begin{align*} Employed_{i,t}&= \alpha_{i}+\omega_{t}+\nu_\tau + \beta Early_i\times New_{i}\times Post_{i,t}+\delta Post_{i,t}\\ &\quad +\gamma New_{i}\times Post_{i,t}+\lambda Early_{i}\times Post_{i,t}+\varepsilon_{i,t}. \end{align*} Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Columns 4, 5, and 6 in Table 4 show the same pattern when employment is defined instead as receiving any positive labor market income during the year. Indeed, Column 4 shows that people in the New regime who defaulted early in the year are 3 percentage points more likely to earn positive labor income, and this effect persists 2 years post-information removal. Furthermore, the probability of receiving positive income from work is positive (and statistically significantly so) and of the same magnitude during the second year (Column 6). The persistence of these effects suggests that default induces a longer-term cost in the labor market, which is consistent with the findings in the labor economics literature that a longer unemployment spell has a persistent effect on future unemployment (e.g., Kroft, Lange, and Notowidigdo 2013).30 In the Internet Appendix, we present regression results using our main specification (i.e., regression (1)), where the outcome variables are lagged by 1 year. These regressions measure effects 1 year before the information is removed, and are akin to a test of pre-trends in a standard difference-in-differences specification. In all cases, the coefficient of interest is not detectably different from zero, formalizing the lack of visible pre-trends in Figure 3 and providing further support to our identification assumption. We explore the impact of credit market information on additional labor market outcomes. Columns 1 to 3 in Table 5 display the output of our main regression model (1), where the postperiod corresponds to 2 years after the removal of the nonpayment flag, for an array of additional labor market outcomes including the log of income from work, log(Wages + 1), the probability of being self-employed, and the log of total post-tax income, log(Income + 1). Income measures are in hundreds of SEK.31 In Column 1 we find that people whose nonpayment flag was retained for less time earn statistically significantly higher wage incomes. Table 5 Wages, income, and self-employment log(Wages + 1) Self employed log(Income + 1) Coefficient (1) (2) (3) $$\beta$$ 0.1995*** –0.0137** 0.1410* (0.077) (0.005) (0.075) Post-period (years) 2 2 2 Obs 63,113 63,113 63,113 $$R^{2}$$ 0.030 0.003 0.040 People 12,664 12,664 12,664 log(Wages + 1) Self employed log(Income + 1) Coefficient (1) (2) (3) $$\beta$$ 0.1995*** –0.0137** 0.1410* (0.077) (0.005) (0.075) Post-period (years) 2 2 2 Obs 63,113 63,113 63,113 $$R^{2}$$ 0.030 0.003 0.040 People 12,664 12,664 12,664 This table shows the effects of credit information on (log)wage income, self-employment, and (log)income, using our main regression model: \begin{align*} Outcome_{i,t}&= \alpha_{i}+\omega_{t}+\nu_\tau + \beta Early_i\times New_{i}\times Post_{i,t}+\delta Post_{i,t}\\ &\quad +\gamma New_{i}\times Post_{i,t}+\lambda Early_{i}\times Post_{i,t}+\varepsilon_{i,t}. \end{align*} Zeros are replaced by 1 in the log outcomes. Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 5 Wages, income, and self-employment log(Wages + 1) Self employed log(Income + 1) Coefficient (1) (2) (3) $$\beta$$ 0.1995*** –0.0137** 0.1410* (0.077) (0.005) (0.075) Post-period (years) 2 2 2 Obs 63,113 63,113 63,113 $$R^{2}$$ 0.030 0.003 0.040 People 12,664 12,664 12,664 log(Wages + 1) Self employed log(Income + 1) Coefficient (1) (2) (3) $$\beta$$ 0.1995*** –0.0137** 0.1410* (0.077) (0.005) (0.075) Post-period (years) 2 2 2 Obs 63,113 63,113 63,113 $$R^{2}$$ 0.030 0.003 0.040 People 12,664 12,664 12,664 This table shows the effects of credit information on (log)wage income, self-employment, and (log)income, using our main regression model: \begin{align*} Outcome_{i,t}&= \alpha_{i}+\omega_{t}+\nu_\tau + \beta Early_i\times New_{i}\times Post_{i,t}+\delta Post_{i,t}\\ &\quad +\gamma New_{i}\times Post_{i,t}+\lambda Early_{i}\times Post_{i,t}+\varepsilon_{i,t}. \end{align*} Zeros are replaced by 1 in the log outcomes. Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. But how large is this earnings effect? In the Internet Appendix we show that running our our main regression in wage levels implies an increase in wages of 3,987 SEK, or roughly $${\$}$$480. Recall from Table 1 that this $${\$}$$480 treatment effect is the result of a reduction in retention time of only 5.5 months. Thus, this cost annualizes to $${\$}$$1,047 per year or $${\$}$$3,142 over the 3 years in which default is flagged publicly. This effect is economically large, approximately 7% of the average annual earnings for people in our sample.32 Recall that improved credit information may also directly increase the amount of credit financial institutions are willing to supply. To get a sense of the relative magnitudes of the earnings and credit supply effects, in the Internet Appendix, we run our main regression using credit outcomes, specifically, the amount of consumer credit and a dummy for any positive consumer credit. We find that the removal of the nonpayment flag leads to an increase in credit of 903 SEK (Column 2), which implies a total annualized effect of $${\$}$$236 in credit per extra year of retention time.33 Thus, the effect of credit information on wages is roughly four times the effect on credit, and suggests that, quantitatively, the labor costs of default may be more important than the loss of access to credit, at least among people at the margins of formality. The wage earnings effect combines the extensive margin effect documented above with an intensive margin effect of higher salaries conditional on employment. We estimate in a back-of-the-envelope calculation that approximately 53% of the earnings effect is driven by the extensive margin.34 These calculations imply important effects on both intensive and extensive margins, which is consistent with the existence of labor market frictions that prevent an adjustment on wages alone.35 In addition to wages, people may also earn incomes from self-employment activities. Column 2 in Table 5 shows that shortened retention times lead to a decrease in self-employment activities. This decrease is despite an increase in the availability of credit, which suggests that many people in our sample use self-employment as a response to unemployment rather than as a high-growth venture.36 Summing across the increase in wage earnings and the decrease in self-employment income, we find an overall increase in post-tax income in Column 3 in Table 5. As an additional robustness test, in the Internet Appendix, we present the results of running our main regression test on a sample where we shift the definition of New and Old regimes 1 year ahead. That is, we define a Placebo New regime as people who defaulted in 2001 and a Placebo Old regime as people who defaulted in 2002, and use $$Employed$$, a dummy for positive wage income, and the log of wages plus one as outcomes. In all 3 cases, the estimated coefficient of interest is not significantly different from zero at conventional levels and even takes the opposite sign to our main results, which supports the assumption that our main results are not driven by differential secular employment trends of defaulters. 2.3 Results by treatment intensity Our identification strategy relies on variation in the retention times of nonpayment information induced by the policy change. To further support our identification, we exploit the bimonthly nature of our credit data and study whether people who were exposed to differential retention times, measured by the time of the year in which they defaulted, experience differential labor market responses. We categorize people in our sample into five groups according to the bimonth in which they defaulted: February–March, April–May, June–July, August–September, and October–November.37 This categorization of default cohorts induces a monotonic ordering of exposure to the policy change, defined as the average reduction in the number of months during which the nonpayment flag was available in the credit registry, for people in the New regime relative to Old regime: the August–September cohort has a 1-month average reduction, June–July has a 3-month average reduction, April–May has a 5-month average reduction, and February–March has a 7-month average reduction. The October–November cohort has, by construction, a 0-month reduction in retention time. We hypothesize that if past arrears affect the probability of being employed, then the measure of months of exposure to the policy, i.e. the number of fewer months in which past arrears are reported, should be positively correlated with the probability of being employed during a given year. To test this hypothesis, we present in Table 6 the results of a regression where we allow the effect of a shorter retention time of past defaults to be linear in the length of exposure, $$Exposuremonths_{i}$$, defined as the reduction in the retention time for the New cohort relative to the Old cohort (i.e., by bimonth of default). \begin{align} 1\left(Wages>0\right){}_{i,t} & =\, \omega_{i} + \omega_{t} + \omega_{\tau} \nonumber \\ &\quad + \beta Exposuremonths_{i}\times New_{i}\times Post_{i,t} \nonumber \\ &\quad + \delta Post_{i,t} + \gamma New_{i}\times Post_{i,t} \nonumber \\ &\quad + \sum_{\tau=1,3,5,7}\lambda_{\tau}1\left(Exposuremonths_{i}=\tau\right)\times Post_{i,\tau} \nonumber \\ &\quad + \varepsilon_{i,t}.\label{eq:linear_effects} \end{align} (2) Table 6 Employment outcomes with varying treatment intensity $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ log(Wages + 1) log(Wages + 1) Coefficient (1) (2) (3) (4) $$\beta$$ 0.0051** 0.0059*** 0.0364*** 0.0398*** (0.002) (0.002) (0.013) (0.013) Post-period (years) 1 2 1 2 Obs 60,891 75,911 60,891 75,911 $$R^{2}$$ 0.007 0.024 0.018 0.030 People 15,232 15,232 15,232 15,232 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ log(Wages + 1) log(Wages + 1) Coefficient (1) (2) (3) (4) $$\beta$$ 0.0051** 0.0059*** 0.0364*** 0.0398*** (0.002) (0.002) (0.013) (0.013) Post-period (years) 1 2 1 2 Obs 60,891 75,911 60,891 75,911 $$R^{2}$$ 0.007 0.024 0.018 0.030 People 15,232 15,232 15,232 15,232 This table shows the output of a regression that estimates the effect of longer retention time of nonpayment flags on the probability of receiving any wage income during the year. The table shows contains the coefficient $$\beta$$ from \begin{align*} 1\left(Wages>0\right){}_{i,t}&=\, \omega_{i} + \omega_{t} + \omega_{\tau} \nonumber\\ &\quad + \beta Exposuremonths_{i}\times New_{i}\times Post_{i,t} \nonumber\\ &\quad + \delta Post_{i,t} + \gamma New_{i}\times Post_{i,t} \nonumber\\ &\quad + \sum_{\tau=1,3,5,7}\lambda_{\tau}1\left(Exposuremonths_{i}=\tau\right)\times Post_{i,\tau} \nonumber\\ &\quad + \varepsilon_{i,t}. \end{align*} There are 15,232 people in this sample instead of 12,664 like in previous tables because we include the June–July cohort of defaulters, a cohort not included in the previous tests to balance people with high and low exposure with the longer retention time. Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 6 Employment outcomes with varying treatment intensity $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ log(Wages + 1) log(Wages + 1) Coefficient (1) (2) (3) (4) $$\beta$$ 0.0051** 0.0059*** 0.0364*** 0.0398*** (0.002) (0.002) (0.013) (0.013) Post-period (years) 1 2 1 2 Obs 60,891 75,911 60,891 75,911 $$R^{2}$$ 0.007 0.024 0.018 0.030 People 15,232 15,232 15,232 15,232 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ log(Wages + 1) log(Wages + 1) Coefficient (1) (2) (3) (4) $$\beta$$ 0.0051** 0.0059*** 0.0364*** 0.0398*** (0.002) (0.002) (0.013) (0.013) Post-period (years) 1 2 1 2 Obs 60,891 75,911 60,891 75,911 $$R^{2}$$ 0.007 0.024 0.018 0.030 People 15,232 15,232 15,232 15,232 This table shows the output of a regression that estimates the effect of longer retention time of nonpayment flags on the probability of receiving any wage income during the year. The table shows contains the coefficient $$\beta$$ from \begin{align*} 1\left(Wages>0\right){}_{i,t}&=\, \omega_{i} + \omega_{t} + \omega_{\tau} \nonumber\\ &\quad + \beta Exposuremonths_{i}\times New_{i}\times Post_{i,t} \nonumber\\ &\quad + \delta Post_{i,t} + \gamma New_{i}\times Post_{i,t} \nonumber\\ &\quad + \sum_{\tau=1,3,5,7}\lambda_{\tau}1\left(Exposuremonths_{i}=\tau\right)\times Post_{i,\tau} \nonumber\\ &\quad + \varepsilon_{i,t}. \end{align*} There are 15,232 people in this sample instead of 12,664 like in previous tables because we include the June–July cohort of defaulters, a cohort not included in the previous tests to balance people with high and low exposure with the longer retention time. Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. The coefficient of interest is $$\beta$$, which measures the average change in the probability of receiving wage income for each month of exposure. As the table shows, 1 month of exposure corresponds to approximately a 0.5% increase in the probability of receiving any wage income and about a 0.4% higher log wage income. This evidence are consistent with the hypothesis that past arrears affect the probability of being employed. As an additional test, in the Internet Appendix we plot the coefficients of a regression where we assign individual dummies to each bimonth of default throughout the year, in effect measuring effects of differential retention time across the bimonth of arrear. Consistent with our identification assumption, the measured effect is stronger for people who experienced greater reductions in retention times because of the month in which their default occurred, although standard errors are relatively large. Further, the pattern is monotonic for 3, 5, and 7 months of exposure. 2.4 Other results: Mobility and education We explore two additional margins that may be affected by changes in credit market information. First, we measure whether increased retention time affects an individual’s geographic mobility within Sweden.38 Because landlords commonly check a prospective lessee’s credit history before signing a lease agreement, we hypothesize that people may be more able to relocate if negative information is held by the credit registry for a shorter period. Moreover, improved access to employment opportunities may also induce mobility. We test this hypothesis in Columns 1 and 2 in Table 7 and define the outcome variable $$Relocates_{i,t}$$ as an indicator for whether an individual moved to a different municipality between years $$t-1$$ and $$t$$. In Column 1, we consider the treatment effect for the entire analysis sample and find that people who experienced a shorter retention time are 1.1 percentage points more likely to move, relative to a baseline mean of 7.7%. Although the coefficient is large in relative terms, it is not statistically significant at standard levels (p-value = .19). Given that people in our sample have very low home ownership rates (9.6%) and that credit checks for residential rental leases are common in Sweden, in column 2, we restrict the sample to the set of people who did not own a home in the preperiod. Here, we find that people who are not home owners are 1.6 percentage points more likely to move across postal codes when their negative credit market information is available to the credit market for less time. While the results are only significant at the 10% level, we find them highly suggestive of a type of mobility lock-in the rental market caused by credit market information.39 Table 7 Additional results: Mobility and education Relocates Relocates Years of schooling Coefficient (1) (2) (3) $$\beta$$ 0.0118 0.0159* –0.0355** (0.009) (0.009) (0.014) Post-period (years) 2 2 2 Sample (at event time 2) Full Nonhomeowners Full Obs 50,229 45,356 60,313 $$R^{2}$$ 0.001 0.001 0.015 People 12,664 11,441 12,414 Relocates Relocates Years of schooling Coefficient (1) (2) (3) $$\beta$$ 0.0118 0.0159* –0.0355** (0.009) (0.009) (0.014) Post-period (years) 2 2 2 Sample (at event time 2) Full Nonhomeowners Full Obs 50,229 45,356 60,313 $$R^{2}$$ 0.001 0.001 0.015 People 12,664 11,441 12,414 This table demonstrates effects of credit market information on household mobility and education. The table contains the coefficients and standard errors for our linear triple difference in difference estimations, using relocates, which is a dummy that equals one if an individual’s residence is in a different county and not missing from the previous event time year, and “years of schooling,” which measures the number of years of education as per the individual’s last completed level of education as outcomes. The number of observations is lower for “relocates” as it is defined in differences from the previous event time year, so the sample period only includes event times 1 through 4 (drops event time 0). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 7 Additional results: Mobility and education Relocates Relocates Years of schooling Coefficient (1) (2) (3) $$\beta$$ 0.0118 0.0159* –0.0355** (0.009) (0.009) (0.014) Post-period (years) 2 2 2 Sample (at event time 2) Full Nonhomeowners Full Obs 50,229 45,356 60,313 $$R^{2}$$ 0.001 0.001 0.015 People 12,664 11,441 12,414 Relocates Relocates Years of schooling Coefficient (1) (2) (3) $$\beta$$ 0.0118 0.0159* –0.0355** (0.009) (0.009) (0.014) Post-period (years) 2 2 2 Sample (at event time 2) Full Nonhomeowners Full Obs 50,229 45,356 60,313 $$R^{2}$$ 0.001 0.001 0.015 People 12,664 11,441 12,414 This table demonstrates effects of credit market information on household mobility and education. The table contains the coefficients and standard errors for our linear triple difference in difference estimations, using relocates, which is a dummy that equals one if an individual’s residence is in a different county and not missing from the previous event time year, and “years of schooling,” which measures the number of years of education as per the individual’s last completed level of education as outcomes. The number of observations is lower for “relocates” as it is defined in differences from the previous event time year, so the sample period only includes event times 1 through 4 (drops event time 0). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Improvements in mobility to better labor markets induced by the removal of bad credit information may have a causal role explaining the employment results. To test for this possibility, we perform a bounding exercise and find that this lock-in effect can explain at most 27% of the baseline effect of information on employment in Table 4.40 Again, the direction of causality may also flow in the opposite direction: a change in employment status may facilitate relocation. Thus, it is likely that mobility is not the main driver of the effects of credit information on employment and wages. Second, we ask whether some people respond to decreased labor market opportunities by adjusting their demand for additional schooling. When wage jobs become more scarce, the opportunity cost of schooling decreases, which may in turn increase the demand for schooling.41 This may be especially true in Sweden, where educational loans do not require credit checks and where the costs of education are relatively low. In Column 3 in Table 7, we find evidence that education is indeed one margin of adjustment used by people. Decreased retention time decreases the number of years of education by 0.0355. While the effect is small in magnitude, it is significant at the 5% level. Taken together, our results provide a consistent characterization of the effects of credit market information on labor markets. We interpret these results as the inverse of our baseline effects: information on past defaults reduces the probability that an individual is and remains employed. People respond to this decrease in employment opportunities by turning to self-employment activities and seeking additional education. As a result, people earn lower wages and lower total incomes 2 years after the information is removed from the credit registry. 3. Mechanisms and Additional Evidence 3.1 Credit information or credit supply? We document an economically large employment cost of default among people on the fringes of the labor and credit markets. Two possible channels could drive this effect. First, in the Internet Appendix, we show that credit supply increases when negative information is deleted.42 Thus, it is possible a priori that such an increase in credit supply might facilitate investments in job search or investment in labor productivity, which may lead to more employment. For example, credit may allow an individual to pay for a car repair, which in turn may improve punctuality at work. Second, employers might use credit information directly to screen workers. While both effects may be at play, we present five pieces of evidence that suggest that employer screening plays a key role above and beyond the role of credit supply in rationalizing our findings. First, recall that the magnitudes of the labor market earnings effects in Section 2.2 are four times larger than the commensurate increase in credit supply. Thus, for the credit effects to explain the entire earnings result, the labor market returns to capital would need to be on the order of 400%, an implausibly high number. Second, recall from Table 5 that improved credit information (and subsequent access to credit) leads to a reduction, rather than an increase, in self-employment activities. This result implies that a subset of people with bad credit records are unconstrained enough to pay any costs required to be self-employed. It seems unlikely that the costs of entering the labor market would be of a larger magnitude. Third, we study how the removal of negative credit information affects the employment of the individual’s spouse. Intuitively, if households are restricted in their access to credit, then a relaxation of credit constraints would also allow an individual’s spouse to supply more labor or invest in becoming more productive at work. At the margin, this would result in more employment for both the individual and the spouse. Although we cannot observe the spouse’s employment directly, for each individual in our sample we observe measures of household disposable income and individual disposable income. At the household and individual levels, disposable income is calculated by our data provider by adding up all income sources and subtracting allowances for dependents (children) and adjusting for the cost of living in a particular area. From these measures, we construct the spouse’s disposable income by subtracting the individual’s disposable income from the household’s disposable income.43 In Columns 1, 2, and 3 in Table 8 we present the output of regression (1) using as outcomes the individual’s disposable income, the household total disposable income, and the spouse’s disposable income, respectively. The spouse’s disposable income can be negative due to government transfers and adjustments, which makes it impossible to use a logarithm plus one approach.44 We restrict the sample of people to those that appear as nonsingle as of event time 2, whose measures of household and individual disposable income are different. Although potentially underpowered, these tests show that the individual’s and household’s disposable incomes increase when their information on past defaults is removed.45 However, Column 3 shows that the spouse’s disposable income does not vary in a statistically significant manner with negative credit information, and, if anything, the point estimate is negative. This evidence suggests that access to credit, brought about through deletion of negative information, does not necessarily relax household-level credit constraints that prevent access to labor markets. This nonresult, which we interpret with caution given potential issues with statistical power, is perhaps even more surprising given that the credit information of spouses is likely correlated due to joint accounts.46 Table 8 Effects on individual’s and spouse’s disposable income Ind. disp. inc. Hh. disp. inc. Spouse disp. inc. log(Ind. disp. inc. +1) log(Hh disp. inc.+1) Coefficient (1) (2) (3) (4) (5) $$\beta$$ 37.27* 34.25 –5.64 0.1204* 0.1466* (20.462) (26.307) (22.802) (0.068) (0.085) Post-period (years) 2 2 2 2 2 Obs 23,154 23,154 23,154 23,154 23,154 $$R^{2}$$ 0.026 0.021 0.002 0.003 0.002 People 4,667 4,667 4,667 4,667 4,667 Ind. disp. inc. Hh. disp. inc. Spouse disp. inc. log(Ind. disp. inc. +1) log(Hh disp. inc.+1) Coefficient (1) (2) (3) (4) (5) $$\beta$$ 37.27* 34.25 –5.64 0.1204* 0.1466* (20.462) (26.307) (22.802) (0.068) (0.085) Post-period (years) 2 2 2 2 2 Obs 23,154 23,154 23,154 23,154 23,154 $$R^{2}$$ 0.026 0.021 0.002 0.003 0.002 People 4,667 4,667 4,667 4,667 4,667 The table shows the regression output of our main regression model (1) using the individual’s disposable income (Column 1), the household’s disposable income (Column 2), and the spouse’s disposable income, calculated as the difference between the household’s and individual’s disposable income (Column 3). Variables are winsorized at the 99th percentile. In Columns 4 and 5, we use the logarithm of the individual’s disposable income and the household’s disposable income respectively, with zeros replace by one. The sample correspond to all people who are not single as of event time 2. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 8 Effects on individual’s and spouse’s disposable income Ind. disp. inc. Hh. disp. inc. Spouse disp. inc. log(Ind. disp. inc. +1) log(Hh disp. inc.+1) Coefficient (1) (2) (3) (4) (5) $$\beta$$ 37.27* 34.25 –5.64 0.1204* 0.1466* (20.462) (26.307) (22.802) (0.068) (0.085) Post-period (years) 2 2 2 2 2 Obs 23,154 23,154 23,154 23,154 23,154 $$R^{2}$$ 0.026 0.021 0.002 0.003 0.002 People 4,667 4,667 4,667 4,667 4,667 Ind. disp. inc. Hh. disp. inc. Spouse disp. inc. log(Ind. disp. inc. +1) log(Hh disp. inc.+1) Coefficient (1) (2) (3) (4) (5) $$\beta$$ 37.27* 34.25 –5.64 0.1204* 0.1466* (20.462) (26.307) (22.802) (0.068) (0.085) Post-period (years) 2 2 2 2 2 Obs 23,154 23,154 23,154 23,154 23,154 $$R^{2}$$ 0.026 0.021 0.002 0.003 0.002 People 4,667 4,667 4,667 4,667 4,667 The table shows the regression output of our main regression model (1) using the individual’s disposable income (Column 1), the household’s disposable income (Column 2), and the spouse’s disposable income, calculated as the difference between the household’s and individual’s disposable income (Column 3). Variables are winsorized at the 99th percentile. In Columns 4 and 5, we use the logarithm of the individual’s disposable income and the household’s disposable income respectively, with zeros replace by one. The sample correspond to all people who are not single as of event time 2. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Fourth, if people changed their job search behavior in response to improved access to credit, then we would expect increases in applications for both credit and jobs in response to the shortened retention time. In the Internet Appendix, we show that credit inquiries do increase following the deletion of negative information. While people are likely to be unaware of the exact timing of their information deletion, credit card companies and other lenders actively pursue people they deem to be creditworthy by monitoring credit records. However, there is no evidence that inquiries by nonfinancial institutions, which include employers, also increase. This evidence is more consistent with credit information affecting the demand for labor rather than the supply of labor. Fifth, and lastly, we exploit the information structure of the credit registries to further unpack the two potential mechanisms. In most countries, members of the credit registry—for example, banks and other financial institutions that share information about their borrowers—have access to all the information that is collected in the credit registry, but nonmembers—for example, employers, telephone and insurance companies and private people—do not.47 This asymmetry in information exists to provide members with incentives to report. Pertinently for our setting, employers cannot observe any details about an individual’s arrears, except whether an active nonpayment flag is present. Whereas banks are able to discriminate between a prospective borrower with ten arrears and a prospective borrower with only one arrear, employers observe identical information for a prospective employee with ten versus one arrear. If having fewer arrears is predictive of better repayment and better job performance, then both lenders and employers should want to use this information when making lending and hiring decisions. However, employers are unable to do so. This implies that in the credit market, people with fewer arrears should have less to gain from arrear flag deletion, while all people with nonpayment flags should experience similar employment screening benefits, regardless of the underlying number of arrears. In Table 9 we measure the credit and employment effects of arrear flag deletion separately for people with an above-median number of arrears and people with a below-median number of arrears. We measure the number of arrears at the time of the last nonpayment, in 2000 or in 2001 depending on the defaulting cohort. In our sample, people with above-median arrears experience the deletion of many arrears in response to the policy change, while people with only one arrear experience the deletion of that singular arrear in response to the policy change. The median number of arrears in the sample is five.48 Columns 1 and 2 in Table 9 show that the effect of the removal of the past nonpayment flag on the probability of receiving any wages is similar for people with many and few arrears. In Column 3 we run the main regression model with full interactions with an indicator for many arrears ($$Many_{i}$$). As expected, the coefficient on the interaction of the main treatment effect with $$Many_{i}$$ is small and insignificant. In contrast, Columns 4 and 5 show that the effect of the removal of the nonpayment flag on credit is positive and significant only for people with many arrears, and Column 6 shows that this difference is large and statistically significant. These patterns are, again, consistent with employer screening effects. If the employment effects were instead due strictly to improved access to credit, then we would expect symmetric patterns in labor and credit outcomes. Table 9 Differential effects by number of arrears $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Consumer Consumer Consumer Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0302* 0.0285* –103.38 967.34*** (0.017) (0.015) (416.697) (338.059) Interaction –0.0016 1,070.73** (0.023) (536.56) Post-period (years) 2 2 2 2 2 2 Sample Few arrears Many arrears All Few arrears Many arrears All Obs 31,346 31,242 63,113 31,767 31,659 62,901 $$R^{2}$$ 0.023 0.017 0.025 0.026 0.020 0.019 People 6,291 6,373 12,664 6,291 6,373 12,664 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Consumer Consumer Consumer Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0302* 0.0285* –103.38 967.34*** (0.017) (0.015) (416.697) (338.059) Interaction –0.0016 1,070.73** (0.023) (536.56) Post-period (years) 2 2 2 2 2 2 Sample Few arrears Many arrears All Few arrears Many arrears All Obs 31,346 31,242 63,113 31,767 31,659 62,901 $$R^{2}$$ 0.023 0.017 0.025 0.026 0.020 0.019 People 6,291 6,373 12,664 6,291 6,373 12,664 This table shows differential effects of credit information on employment and credit by the number of arrears at default. The table shows the regression output of our main regression model (1) for different subsamples. Columns 1 and 4 restrict the sample to people who had the median (five) or less arrears at the time of the last default, and Columns 2 and 5 restrict the sample to those with more arrears than the median. Columns 3 and 6 use the entire sample and run the main regression model Equation (1) where all right-hand-side variables are interacted with a dummy that equals one for people with many arrears at the time of the last nonpayment. Outcomes include $$1(wages>0)$$, a dummy for positive wages, and consumer, which measures the level of consumer credit in Swedish Kronor. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 9 Differential effects by number of arrears $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Consumer Consumer Consumer Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0302* 0.0285* –103.38 967.34*** (0.017) (0.015) (416.697) (338.059) Interaction –0.0016 1,070.73** (0.023) (536.56) Post-period (years) 2 2 2 2 2 2 Sample Few arrears Many arrears All Few arrears Many arrears All Obs 31,346 31,242 63,113 31,767 31,659 62,901 $$R^{2}$$ 0.023 0.017 0.025 0.026 0.020 0.019 People 6,291 6,373 12,664 6,291 6,373 12,664 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Consumer Consumer Consumer Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0302* 0.0285* –103.38 967.34*** (0.017) (0.015) (416.697) (338.059) Interaction –0.0016 1,070.73** (0.023) (536.56) Post-period (years) 2 2 2 2 2 2 Sample Few arrears Many arrears All Few arrears Many arrears All Obs 31,346 31,242 63,113 31,767 31,659 62,901 $$R^{2}$$ 0.023 0.017 0.025 0.026 0.020 0.019 People 6,291 6,373 12,664 6,291 6,373 12,664 This table shows differential effects of credit information on employment and credit by the number of arrears at default. The table shows the regression output of our main regression model (1) for different subsamples. Columns 1 and 4 restrict the sample to people who had the median (five) or less arrears at the time of the last default, and Columns 2 and 5 restrict the sample to those with more arrears than the median. Columns 3 and 6 use the entire sample and run the main regression model Equation (1) where all right-hand-side variables are interacted with a dummy that equals one for people with many arrears at the time of the last nonpayment. Outcomes include $$1(wages>0)$$, a dummy for positive wages, and consumer, which measures the level of consumer credit in Swedish Kronor. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. The findings illustrate that banks likely adjust their underwriting decisions according to the severity of an individual’s past defaults. In contrast labor markets are unable to do so and are forced to pool all people with a nonpayment flag. Unless the information contained in the number of arrears is relevant for banks but not for employers, then the labor cost of default imposed by credit information may be excessive for those people with few arrears, for example. Information asymmetry provided to credit and noncredit market participants may lead to inefficiency. Given that credit registries were largely designed to reduce information asymmetries in the credit market, their use in labor markets is likely only second best. 3.2 Incidence We end our analysis by asking, for which types of people are the employment effects of negative credit information strongest? This question is relevant both for policy makers and for academics learning about what the credit score may convey to employers. First, we study how the effects vary for people with different levels of education. In Table 10 we present results for two subsamples: people with 11 or fewer years of completed schooling (the median number of years of schooling), and people with more than 11 years of schooling. Columns 1 and 2 show that a shorter retention time strongly increases the probability of employment for people with little education, but it has almost no effect on people with many years of schooling (p-value of difference .035). Columns 3 and 4 show that this pattern is repeated for log wages (p-value of difference .095). Thus, the employment impact of negative credit information is felt more acutely by those with lower levels of education. Table 10 Heterogeneity by preperiod education levels $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$\log(Wages+1)$$ $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0440*** –0.0003 0.2982*** 0.0102 (0.013) (0.021) (0.091) (0.147) Post-period (years) 2 2 2 2 Sample (years) $$\leq11$$ $$>11$$ $$\leq11$$ $$>11$$ Obs 44,543 16,240 44,543 16,240 $$R^{2}$$ 0.022 0.042 0.029 0.051 People 8,914 3,249 8,914 3,249 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$\log(Wages+1)$$ $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0440*** –0.0003 0.2982*** 0.0102 (0.013) (0.021) (0.091) (0.147) Post-period (years) 2 2 2 2 Sample (years) $$\leq11$$ $$>11$$ $$\leq11$$ $$>11$$ Obs 44,543 16,240 44,543 16,240 $$R^{2}$$ 0.022 0.042 0.029 0.051 People 8,914 3,249 8,914 3,249 This table shows differential effects of credit information on employment depending on preperiod level of education. The table shows the regression output of our main regression model (1) for different subsamples: people with 11 or fewer completed years of schooling, and people with more than 11 years of schooling. Outcomes are positive wage income and $$\log(Wages+1)$$, where zeros have been replaced by 1, as defined previously. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 10 Heterogeneity by preperiod education levels $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$\log(Wages+1)$$ $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0440*** –0.0003 0.2982*** 0.0102 (0.013) (0.021) (0.091) (0.147) Post-period (years) 2 2 2 2 Sample (years) $$\leq11$$ $$>11$$ $$\leq11$$ $$>11$$ Obs 44,543 16,240 44,543 16,240 $$R^{2}$$ 0.022 0.042 0.029 0.051 People 8,914 3,249 8,914 3,249 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$\log(Wages+1)$$ $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0440*** –0.0003 0.2982*** 0.0102 (0.013) (0.021) (0.091) (0.147) Post-period (years) 2 2 2 2 Sample (years) $$\leq11$$ $$>11$$ $$\leq11$$ $$>11$$ Obs 44,543 16,240 44,543 16,240 $$R^{2}$$ 0.022 0.042 0.029 0.051 People 8,914 3,249 8,914 3,249 This table shows differential effects of credit information on employment depending on preperiod level of education. The table shows the regression output of our main regression model (1) for different subsamples: people with 11 or fewer completed years of schooling, and people with more than 11 years of schooling. Outcomes are positive wage income and $$\log(Wages+1)$$, where zeros have been replaced by 1, as defined previously. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. One possible interpretation of this heterogeneity is that past credit information is only one of many signals used by employers to infer an individual’s unobserved productivity. For well-educated people, this information may be less relevant than other types of information (such as experience), and as such it may be down-weighted by employers. People with little formal education may also have fewer ways to signal their types.49 Second, we explore whether the effects differ by employment history, namely the preperiod (event time 2) employment status.50 Both the previously unemployed and previously employed may experience negative impacts. For example, negative credit information may hinder the ability of unemployed people to find work. This might also be the case for the many underemployed and part-time workers coded as previously employed in our sample.51 However, people with long prior unemployment spells may already be severely handicapped in the labor market (e.g., Kroft, Lange, and Notowidigdo 2013), even in the absence of negative credit information, and may have stopped their active job search. Thus, the additional impact of negative credit market information may be muted for this group. In Columns 1 and 2 in Table 11, we run our main specification (1) separately for those employed and unemployed at event time 2 (i.e., the year before arrear removal), respectively. We find similar positive effects on wage employment and on log wages for both groups (these results are statistically indistinguishable). In Columns 3 and 4, we further subdivide the previously unemployed into chronically and nonchronically unemployed. We define the chronically unemployed to be those without employment at event time 2 and who additionally worked at most 1 year out of the the 3 pre-period years. We find that the effects on formal employment and $$\log(Wages + 1)$$ are relatively small in magnitude (indeed, indistinguishable from zero) for the chronically unemployed, while the effects are large in magnitude for the nonchronically unemployed (p-value of difference on $$\log(Wages + 1)$$ .114). While underpowered, the differences in magnitudes are nonetheless striking. These results suggest that credit information may be most informative when people do not have other ways to signal their productivity. Long unemployment spells may provide employers with information that makes credit records superfluous. Table 11 Heterogeneity by preperiod employment history Panel A: $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0336** 0.0319* 0.0196 0.0578* (0.014) (0.016) (0.019) (0.030) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.050 0.016 0.009 0.065 People 5,424 6,942 4,819 2,123 Panel B: $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.2704** 0.1970* 0.0761 0.4505** (0.109) (0.107) (0.124) (0.202) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.072 0.018 0.014 0.067 People 5,424 6,942 4,819 2,123 Panel A: $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0336** 0.0319* 0.0196 0.0578* (0.014) (0.016) (0.019) (0.030) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.050 0.016 0.009 0.065 People 5,424 6,942 4,819 2,123 Panel B: $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.2704** 0.1970* 0.0761 0.4505** (0.109) (0.107) (0.124) (0.202) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.072 0.018 0.014 0.067 People 5,424 6,942 4,819 2,123 This table shows differential effects of credit information on employment depending on preperiod employment status. The table shows the regression output of our main regression model (1) for different subsamples. In panels A and B, Column 1 restricts the sample to people who are employed ($$Employed_{i,t}=1$$) as of event time 2, the year before their information on nonpayments is removed. Column 2 restricts the sample to people who are unemployed as of event time 2. Columns 3 and 4 split the sample of unemployed people. Column 3 restricts the sample to people who are chronically unemployed as of event time 2, defined as those people who have been unemployed for 2 or more years in the 3-year preperiod. Column 4 restricts to unemployed people who are not chronically unemployed. Panel A uses a dummy for positive wage income as outcome. Panel B uses $$\log(Wages + 1)$$, where zeros have been replaced by 1, as outcome. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 11 Heterogeneity by preperiod employment history Panel A: $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0336** 0.0319* 0.0196 0.0578* (0.014) (0.016) (0.019) (0.030) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.050 0.016 0.009 0.065 People 5,424 6,942 4,819 2,123 Panel B: $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.2704** 0.1970* 0.0761 0.4505** (0.109) (0.107) (0.124) (0.202) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.072 0.018 0.014 0.067 People 5,424 6,942 4,819 2,123 Panel A: $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0336** 0.0319* 0.0196 0.0578* (0.014) (0.016) (0.019) (0.030) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.050 0.016 0.009 0.065 People 5,424 6,942 4,819 2,123 Panel B: $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.2704** 0.1970* 0.0761 0.4505** (0.109) (0.107) (0.124) (0.202) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.072 0.018 0.014 0.067 People 5,424 6,942 4,819 2,123 This table shows differential effects of credit information on employment depending on preperiod employment status. The table shows the regression output of our main regression model (1) for different subsamples. In panels A and B, Column 1 restricts the sample to people who are employed ($$Employed_{i,t}=1$$) as of event time 2, the year before their information on nonpayments is removed. Column 2 restricts the sample to people who are unemployed as of event time 2. Columns 3 and 4 split the sample of unemployed people. Column 3 restricts the sample to people who are chronically unemployed as of event time 2, defined as those people who have been unemployed for 2 or more years in the 3-year preperiod. Column 4 restricts to unemployed people who are not chronically unemployed. Panel A uses a dummy for positive wage income as outcome. Panel B uses $$\log(Wages + 1)$$, where zeros have been replaced by 1, as outcome. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Finally, in the Internet Appendix, we show that the employment effect of shorter retention times is concentrated in geographical areas with low unemployment. Although again the test may be underpowered, one interpretation of this result is that the employment cost of default is more severe for “bad” people in “good times” (i.e., low unemployment areas) than for average households in high unemployment areas. Further, it is possible that the signal of productivity provided by credit information becomes more valuable when labor markets are tighter. 52 4. Conclusion We combine a unique natural experiment in Sweden with detailed credit and labor market data to document that credit market information has economically important effects that spill over onto other domains of a borrower’s life, namely success in the labor market. We focus on a marginal population, one that is likely to experience financial distress and unemployment, for whom exclusion from the credit and labor markets is likely quite costly, and to whom policy makers tend to pay close attention. We find robust evidence that an earlier deletion of negative credit information makes people more likely to be employed, and as a result, they earn higher incomes. These results highlight an understudied interlinkage between credit and labor markets. These results complement and contrast with findings by Cohen-Cole, Herkenhoff, and Phillips (2016b) and Dobbie et al. (2016), suggesting the effects of bad credit records are likely to be heterogeneous and depend on the type of credit information being reported and on the population under study. We also show that when labor market opportunities become scarce, people seek out self-employment and schooling as alternatives. These results indicate that for our sample of low income Swedes, self-employment is often an inferior alternative to the wage labor market. This finding resonates with the narrative in the entrepreneurship literature that many businesses owned by low income groups are not primed for transformative growth. The schooling response to the unemployment caused by negative credit information is also consistent with prior literature. While credit supply is also responsive to the deletion of negative credit information, we further provide evidence that a large portion of our estimated effects is likely explained by employer screening, a practice that has increased dramatically over the past decade and that has garnered the attention of many policy makers. Our results present some of the first causal evidence that in vulnerable populations, negative credit information can indeed impede success in the labor market. This implies that a temporary shock that causes an individual to default may have lasting and profound consequences. These results also imply that damage from credit information errors may be amplified through the labor market channel.53 Further, it may be difficult for households to use labor supply to smooth consumption when their credit record is poor. We also find suggestive evidence that asymmetries in the information available to noncredit entities may cause inefficiencies in the use of credit information. Our paper estimates the employment costs of default for a particularly vulnerable population, which is an important input for for modeling unsecured credit markets (e.g., Chatterjee et al. 2007; Livshits, MacGee, and Tertilt 2007) and for the policy debate. On these vulnerable populations, credit information could induce multiplier effects on unemployment (e.g., duration dependence) and potentially lead to poverty traps (Banerjee and Duflo 2012; Kroft, Lange, and Notowidigdo 2013). However, we acknowledge that a full welfare analysis of employer credit screening policies requires many additional inputs and several questions remain unanswered. For example, what are the countervailing benefits from using credit information on the efficiency of matching between firms and employees? Does the employment cost of default strengthen repayment incentives and result in deeper financial markets?54 These are all important questions for future work. Some contemporaneous studies have begun to address these questions. For example, Balance, Clifford, and Shoag (2016) show that state-level bans on credit checks by employers increased employment but caused a deterioration of labor market outcomes of particularly vulnerable populations. Bartik and Nelson (2016) and Cortes, Glover, and Tasci (2016) exploit the same regulation changes to find evidence of an average deterioration of labor markets, particularly for minorities, coupled with an increased demand from employers for alternative signals of applicants’ productivity, such as education. These studies suggest that banning the use of credit information in hiring decisions may harm the labor market outcomes of vulnerable populations and potentially reduce welfare. While we do not attempt such a welfare analysis, our results can provide guidance to policy makers regarding other types of interventions that might or might not limit the negative labor market consequences from experiencing a negative shock. We find very little evidence to indicate that access to credit alone dramatically improves access to labor markets. This suggests that policies such as social transfers or subsidized government credit would be unlikely to lead to large employment benefits. Instead, policy makers might want to consider policies that either help people to improve their credit records, such as credit counseling, or that help people to improve the noncredit information that they can report to prospective employers. Our results suggest that negative credit information is most detrimental for those workers with fewer alternate signals that employers can use for screening.55 We thank the editor Andrew Karolyi; the anonymous referees; Manuel Adelino, Tony Cookson, Nathan Hendren, Andrew Hertzberg, Wei Jiang, Emi Nakamura, Matthew Notowidigdo, Daniel Paravisini, Thomas Philippon, Enrique Seira, Nicolas Serrano-Velarde, Jose Tessada, Daniel Wolfenzon, and Jonathan Zinman; and numerous seminar and conference participants for helpful comments. Jesper Böjeryd provided excellent research assistance. Funding from VINNOVA is gratefully acknowledged. All errors are our own. Marieke Bos is also a visiting scholar at the Federal Reserve Bank of Philadelphia. The views expressed here are those of the authors and do not necessarily represent those of the Federal Reserve Bank of Philadelphia, or the Federal Reserve System. Supplementary data can be found on The Review of Financial Studies web site. Footnotes 1 For example, see Musto (2004), Brown and Zehnder (2007), Djankov, McLiesh, and Shleifer (2007), De Janvry, McIntosh, and Sadoulet (2010), Bos and Nakamura (2014), González-Uribe and Osorio (2014), Liberman (2016), and Dobbie et al. (2016). 2 In the United States, 47% of firms check the credit information of prospective employees (see http://www.shrm.org/research/surveyfindings/articles/pages/creditbackgroundchecks.aspx). In Sweden, where we conducted our empirical analysis, the leading credit registry estimates that roughly 15% of all the inquiries it receives are made by nonfinancial institutions conducting background checks on potential employees. These nonfinancial institutions employ approximately 37% of the Swedish labor force. On its Web site, the Swedish Government Employment Agency lists jobs that currently require a clean credit record: financial, transportation, real estate, retail, and security (see http://www.arbetsformedlingen.se). 3 Arrears, in turn, are inputs into the credit score. However, nonfinancial actors typically receive only a strict subset of the information housed in the credit registry and are not able to observe the credit score. In the United States, employers are not allowed to observe the FICO score or any other aggregated score. In Sweden, employers cannot see the summary credit score or other key details about the nature of the past delinquencies, but importantly, they do observe the nonpayment flag. 4 Screening by landlords may also contribute to the causal effect of information on employment by affecting mobility. We perform a bounding exercise and show that increased mobility following the removal of credit information can explain at most a quarter of the magnitude of our results. 5 See, for example, Karlan and Zinman (2009), Mullainathan and Shafir (2013), and Kehoe, Midrigan, and Pastorino (2016). 6 See Chatterji and Seamans (2012), Hombert et al. (2014), Greenstone, Mas, and Nguyen (2014), Schmalz, Sraer, and Thesmar (2017), and Adelino, Schoar, and Severino (2015). 7 See Low (2005), Pijoan-Mas (2006), Jayachandran (2006), and Blundell, Pistaferri, and Saporta-Eksten (2016). 8 Our results on the extensive margin of employment are also inconsistent with those of Herkenhoff (2013) and Cohen-Cole, Herkenhoff, and Phillips (2016a), who study a matching model of the labor market, where access to credit leads to higher unemployment through an increase in the employee’s outside option. Their model also suggests that wages are higher conditional on employment, a test we do not pursue given that conditioning on employment most likely leads to a selection bias in our setting. 9 We also find that our main effects are stronger among people with fewer years of schooling, consistent with a model in which employers choose to weigh multiple signals of productivity differentially. 10 That banks and nonfinancial institutions, like employers, have access to different sets of information is a prevalent feature of credit registries around the world, an asymmetry that arises to provide banks with incentives to report (Pagano and Jappelli 1993). 11 Aside from the empirical evidence cited above, theoretical contributions to this literature include Pagano and Jappelli (1993), Padilla and Pagano (2000), and Elul and Gottardi (2015), among others. 12 See, for example, Dobbie and Song (2015) and Liberman (2016). 13 For the policy debate, see, for example, the epigraph and Senator Elizabeth Warren and Representative Steve Cohen’s op-ed at http://webcache.googleusercontent.com/search?q=cache:http://blog.credit.com/2015/09/sen-warren-rep-cohen-its-time-to-stop-employer-credit-checks-125468/&gws_rd=cr&dcr=0&ei=bYwqWsa7GrLN6QS-rpfIBg. 14 Swedish banks typically report borrower default at 90 days past due. Other entities such as phone companies exercise discretion when a consumer is reported as delinquent. People have the option of filing an appeal to the courts to correct potential errors. 15 In particular, the law states that credit records are available to other parties as long as the explicit intent is to enter into a contractual relationship. Furthermore, a copy of their credit record and the identity of the requesting party is sent automatically to the individual whose information is requested. 16 The Swedish government announced their decision to change Paragraph 8 of the law that regulates the handling of credit information (KreditUpplysningsLagen or credit inquiry law) on July 2003, and the law change took effect in October 2003. See http://rkrattsdb.gov.se/SFSdoc/03/030504.PDF 17 In our bimonthly data, an individual who received an arrear on December 1 but had that arrear removed on December 31, is first observed without an arrear in February, 3 years later. 18 For example, people who lose their jobs and remain unemployed may have a higher propensity to default on their debts (Foote, Gerardi, and Willen (2008) and Gerardi et al. 2013). Further, loan repayment and job performance may both be affected by traits such as responsibility and trustworthiness. 19 Evidence consistent with this fact is presented graphically in the Internet Appendix. We plot the average probability of receiving any wages 2 years after their last default by the bimonth of default, for people in our sample who defaulted in 2000 or in 2001. The probability of employment varies between a max of 85% for February–March defaulters to a low of 77% for October–November defaulters. 20 See Bos, Carter, and Skiba (2012) for an extensive discussion of the household characteristics of pawn borrowers in Sweden compared with the full Swedish population and for a comparison of pawn borrowers in Sweden and in the United States. 21 Some people in our sample obtained a new arrear after this 20-month period. Thus, they maintain a nonpayment flag in their records after the original arrear received in 2000 or in 2001 is removed, which reduces the power of our tests. 22 The credit registry updates its information on a daily basis. The research team, however, was only allowed access to bimonthly snapshots of the data. 23 To make the early and late groups comparable in size, we exclude the June–July cohort. However, below we include people in this cohort when we measure differential effects by differential intensity of the treatment by month of nonpayment. 24 All our outcomes are at the yearly level, and any baseline variation in these levels that is driven by macroeconomic shocks is absorbed by the year fixed effects, $$\omega_{\tau}$$. 25 See http://www.statistikdatabasen.scb.se/pxweb/sv/ssd/START__LE__LE0101__LE0101S/LE01012013S22/?rxid=91289227-eae0-41b9-8da5-d9e7bbcf5e66. 26 See http://www.statistikdatabasen.scb.se/pxweb/sv/ssd/START__AM__AM0208__AM0208B/YREG26/?rxid=f45f90b6-7345-4877-ba25-9b43e6c6e299. 27 See http://www.arbetsformedlingen.se. 28 In the Internet Appendix we present plots of the average evolution of each outcome without differencing, that is, Old-Early, Old-Late, New-Early, and New-Late. 29 In the Internet Appendix we present a robustness result in which we exclude the individual fixed effects. Results are slightly larger in magnitude but are essentially unchanged from our main test. 30 Because of the panel nature of the data, we cluster standard errors at the individual level to avoid serial autocorrelation. One potential concern is that standard errors are serially correlated across bimonths of default. In the Internet Appendix, we present estimates of regression (1) using standard errors clustered at the bimonth of default by 5-year preperiod age groups (52 clusters). The significance is essentially unchanged relative to the main specification. 31 In the Internet Appendix we present the results of specifications with alternative transformations of the dependent variable (1) using the hyperbolic sine transformation as an alternative to replacing zeros in the logarithm and (2) using the level of wages. 32 We also find that the impacts on credit are short-lived and only last 1 year, while the earnings impacts persist across (at least) 2 years. 33 This corresponds to a 48% effect size on consumer credit (mean 1,879 SEK). In the preperiod, 75% of people in our sample have no consumer credit, likely from their negative credit information. 34 We obtain this fraction as follows. First, the average wage of people who transitioned from zero wages to positive wage income in event time 2, the year before the past default flag is removed, is 71,200 SEK. Thus, a 3% extensive margin effect from Column 4 in Table 4 corresponds to a wage effect of 2,129 SEK. Thus, the extensive margin represents $$\frac{2,129}{3,987}=53.4\%$$ of the total wage effect of 3,987 SEK shown in the Internet Appendix. 35 For example, the typically high level of unionization in Sweden contributes to a limited scope for adjustment along the wage margin. For statistics on the trade union density in Sweden, see, for example, https://stats.oecd.org/Index.aspx?DataSetCode=UN_DEN. 36 See Banerjee et al. (2015) for an application of this idea in India. 37 In this section, the sample includes people who defaulted in the June–July bimonth, an addition that increases the number of people and observations relative to previous tests. 38 In unreported results, we study the effect of negative credit information on the propensity of people in our sample to relocate. Consistent with past arrears reducing labor market opportunities, we find that people are slightly less likely to leave the country following the early deletion of their past defaults, although the effect is small. 39 This pattern is similar to the housing lock-in documented by Struyven (2014), who studies Dutch homeowners with high loan-to-value ratios. 40 We estimate this fraction as follows. We repeat the mobility regression result conditioning on people who moved and changed employment status, which implies a coefficient of 0.8%. If we fully attribute this coefficient to the causal effect of increased mobility following the early removal of credit information, then mobility can explain up to $$\frac{0.8\%}{3\%}=27\%$$ of the baseline effect on employment (denominator taken from Column 4 in Table 4). 41 See Charles, Hurst, and Notowidigdo (2015) for evidence of this idea in the United States. 42 In particular, we run our main specification (regression (1)), where the outcomes are $$1\left(Consumer>0\right)$$, a dummy for any consumer credit, and $$Consumer$$, the level of consumer credit. In both, the coefficient of interest is positive and highly significant. 43 We winsorize each of these variables at the 99th percentile. 44 These specifications using levels are comparable to the one we present in Table IAV (see the Internet Appendix) using wage as the outcome. 45 For comparability with our previous results, we present estimates using the logarithm of individual and household disposable income plus one on Columns 4 and 5 in Table 8 and note strongly significant effects of the removal of past of defaults on these outcomes, consistent with the evidence in the previous section. 46 Thus, it is possible that a spouse actually increases labor supply when the individual is unable to find a job because of negative credit information (Blundell, Pistaferri, and Saporta-Eksten 2016). 47 In the Internet Appendix, we include a figure that illustrates what information is available to members and nonmembers in Sweden. 48 We recognize that the number of arrears is not randomly assigned and may be correlated with other types of heterogeneity. Nonetheless, we find the results highly suggestive. 49 Low levels of education may also be correlated with other measures of labor market opportunities, such as industry or type of job. It might also be possible that different types of employers are more or less likely to use credit information when making hiring decisions. 50 We would have liked to explore other characteristics of an individual’s employment history. However, Statistics Sweden was unwilling to match other job characteristics such as type of job or industry of the employer to our credit information data set. 51 Our data set does not allow us to differentiate part-time from full-time employment. 52 It may also be the case that idiosyncratic shocks are punished more severely than are aggregate shocks. 53 For example, see http://www.forbes.com/sites/halahtouryalai/2013/12/17/should-your-credit-score-matter-on-job-interviews-senator-warren-says-no-aims-to-ban-employer-credit-checks/. 54 For example, people may want to continue to service underwater mortgages if the labor market costs are sufficiently high. Extrapolating to a different market and context, labor market costs may help to explain why strategic default was not common during the housing crisis (Foote, Gerardi, and Willen 2008). 55 These findings are consistent with those of Pallais (2014), who measures benefits to future employment from certification by previous employers in an online labor market. References Adelino, M., Schoar, A. and Severino. F. 2015 . House prices, collateral, and self-employment. Journal of Financial Economics 117 : 288 – 306 . Google Scholar CrossRef Search ADS Balance, J., Clifford, R. and Shoag. D. 2016 . “No more credit score” employer credit check banks and signal substitution. Working Paper . Banerjee, A., Breza, E. Duflo, E. and Kinnan. C. 2015 . Do credit credit constraints limit entrepreneurship? heterogeneity in the returns to micronance. Working Paper . Banerjee, A., and Duflo. E. 2012 . Poor economics: A radical rethinking of the way to ght global poverty . 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The Labor Market Effects of Credit Market Information

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Oxford University Press
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© The Author(s) 2018. Published by Oxford University Press on behalf of The Society for Financial Studies. All rights reserved. For Permissions, please e-mail: journals.permissions@oup.com.
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0893-9454
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Abstract

Abstract We exploit a natural experiment to provide one of the first measurements of the causal effect of negative credit information on employment and earnings. We estimate that one additional year of negative credit information reduces employment by 3 percentage points and wage earnings by $${\$}$$1,000. In comparison, the decrease in credit is only one-fourth as large. Negative credit information also causes an increase in self-employment and a decrease in mobility. Further evidence suggests this cost of default is inefficiently borne by those most creditworthy among previous defaulters. Received April 5, 2017; editorial decision September 2, 2017 by Editor Andrew Karolyi. Authors have furnished an Internet Appendix, which is available on the Oxford University Press Web Site next to the link to the final published paper online. Credit registries are an important tool used by lenders worldwide to obtain better information about borrowers and to strengthen repayment incentives. Several studies have documented that credit information affects borrowers’ access to credit.1 However, much less is known about the effects of credit information on noncredit outcomes such as employment that are critical for welfare and policy analysis. Credit information may affect employment indirectly through its effects on credit supply, but more direct channels are also possible. Indeed, while credit registries were largely established to improve the efficiency of credit markets, over time, noncredit actors have increasingly sought out their information (e.g., insurance companies, utilities, landlords, and mobile phone providers). Ample anecdotal (and some survey) evidence shows that many employers around the world also query credit registries when making hiring decisions.2 In this paper we provide one of the first measurements of the causal effect of negative credit information on employment and earnings. To do this, we obtain detailed tax, employment, and demographic records merged with data from the Swedish credit registry for a sample of people drawn from the universe of pawn-loan borrowers in Sweden. This sample is well suited to measure the employment effects of credit information because it is formed by people who are exposed both to financial distress and to frequent spells of unemployment. As a result, people in our sample are more weakly attached to the labor market and are likely to bear any employment cost of negative credit information, should this cost exist. In Sweden, like in most countries (e.g., Miller (2000)), information on the past repayment of debts and other obligations is collected and disseminated through credit registries, and mostly used by lenders to evaluate new borrowers. A borrower who defaults in Sweden receives an arrear in her file, and a nonpayment flag appears prominently on the top of the credit report.3 Swedish law mandates that each arrear must be deleted from an individual’s credit record 3 years after it was registered. In turn, the nonpayment flag at the top of the report remains until all arrears have expired. Our objective is to measure the causal effect on employment of having a past arrear reported in the credit record. However, a simple comparison of people with and without reported past arrears is likely to provide biased estimates of the causal effect of interest, as people with past arrears are more likely to be unemployed, independent of the nature of their credit information. To identify the causal effect, we exploit a policy change that varied the amount of time that arrears were reported by the credit registry in Sweden. Before October 2003, arrears were deleted on the last calendar day (i.e., December 31) of the third year after first being recorded. Beginning in October 2003, the law was reinterpreted and arrears were deleted exactly 3 years to the day after they were registered. We refer to the 2001 cohort of defaulters in our sample as the New regime and the 2000 cohort of defaulters as the Old regime. The policy change caused a decrease in the average retention time of past defaults for members of the New regime relative to the Old regime. Importantly, given that the policy change was announced in March 2003, all people who defaulted in 2000 or in 2001 did so under the same beliefs about the retention time of their flags of past defaults. Importantly for identification, the key impetus for this change was technological and coincided with an upgrade of the computer systems used by the registry. This policy change was first exploited by Bos and Nakamura (2014). We use the variation in the retention of past arrears induced by the policy change to identify the causal effect of negative credit information on employment outcomes. However, a simple comparison of people in the New and in the Old regime before and after the removal of their respective nonpayment flags would confound any causal effect of credit information with other annual trends in the Swedish economy. Instead, we take advantage of the fact that the policy change modified the retention time of the indicator of past defaults differentially for people who defaulted in different calendar months across the year. In particular, among people who received an arrear early in the year, those in the Old regime had a longer retention time than those in the New regime. In contrast, people in the New and Old regimes with an arrear late in the year faced the same retention time. Thus, in our main empirical strategy we compare the yearly employment outcomes of people in the New and Old regimes who received a nonpayment flag early in the year with those who received one late in the year and track how these outcomes change after the nonpayment flag is deleted. We find that the deletion of past defaults has large effects on employment. An individual in the New regime who defaulted early in the calendar year is approximately 3 percentage points more likely to be employed the year in which her nonpayment information is removed from the credit registry, relative to an individual in the Old regime and relative to an individual who defaulted late in the year. This difference persists (at least) 1 year after the information is deleted, albeit with a smaller magnitude. People whose information is removed earlier also earn higher wages and incomes, are less likely to pursue additional years of education, and are more likely to change residence. Moreover, people most exposed to the policy are less likely to be self-employed, suggesting that for our population of alternative borrowers, entrepreneurship acts more as a response to involuntary unemployment and less as a high-growth business opportunity. We estimate that removing an individual’s past nonpayment flag 1 year earlier raises yearly wages by approximately $${\$}$$1,000, an effect that is four times larger than the increase in consumer credit. Credit information may affect employment through two channels. First, as discussed above, employers may use credit information directly to screen employees.4 Second, improved credit information increases an individual’s access to credit, which may in turn impact employment in many ways. For example, more credit may allow people to make investments necessary for finding or keeping a job.5 Increased credit may also allow people to invest in entrepreneurship, thus reducing the relative value of wage labor.6 Further, if people use labor hours to smooth negative shocks in a precautionary manner, they may reduce their labor supply following an increase in access to credit.7 Distinguishing between these two mechanisms is important insofar as the policy responses that emerge from each are very different. Our baseline results rule out effects predominantly arising from the entrepreneurship and labor smoothing channels, by which more access to credit would lead to more wage employment.8 We exploit rich household-level data to provide two additional tests that suggest that employer screening is the main driver of our results. First, we study intra-household effects of nonpayment flag removal. If credit constraints impede a household’s labor supply, then we should expect employment effects on both the individual whose information is deleted and the spouse’s. However, we find no detectable treatment effect on the income of the spouse. Second, we explore differences in the information available to financial institutions versus employers. Crucially, employers are only able to observe a strict subset of the lender’s information. In particular, lenders can observe the number of arrears, while employers can only observe the presence of at least one arrear. We find that access to credit increases upon removal of the nonpayment flag but only for people who have many (above median) arrears removed from their record together with the nonpayment flag. There is no increase in credit upon removal of the nonpayment flag for people with few arrears. In contrast, we find that the effect of the removal of the past default flag on employment is positive, similar in magnitude, and statistically indistinguishable for people with many or few arrears.9 With the caveat that the sources of heterogeneity are not randomly determined and could thus reflect unobserved differences in labor market opportunities across groups, we view these results as broadly inconsistent with a model in which employment is mainly determined by differences in access to credit. This latter result also suggests a potential inefficiency in the use of credit market information by employers. Indeed, one possible interpretation of this result is that banks use all of the available information in their underwriting policies and recognize that borrowers with few arrears are more creditworthy. However, employers are forced to pool people with few or many arrears, leading to a uniform increase in employment post-deletion. Unless the information contained in past repayment behavior that is relevant for banks is not relevant for employment, such pooling disadvantages people with fewer initial arrears and also likely disadvantages firms.10 In summary, our contribution is threefold. First, we document and measure a large employment cost of default associated with credit information among people at the margins of formality. Second, our results suggest that this employment cost of default is largely driven by employer screening. Third, we show suggestive evidence that this employment cost of default is inefficiently borne by creditworthy people. Our paper contributes to a recent academic literature that provides mixed evidence of the employment effect of credit information. Cohen-Cole, Herkenhoff, and Phillips (2016b) document an increased flow into and out of self-employment after removal of the bankruptcy flag from credit records in the United States, while Dobbie et al. (2016) estimate that the removal of bankruptcy flags has no effect on employment. There are two key reasons why our results could differ from Dobbie et al. (2016). First, we focus on different types of credit information. While past defaults, which are our focus, can only be observed through credit reports, bankruptcies remain in the public record and can potentially be accessed by employers or job search agencies even when they have been deleted from credit records. Second, the timing of the credit information differs between the two papers. Past defaults in our setting are at most 3 years old, while bankruptcy flags are removed 7 or 10 years after filing. One interpretation of these different results is that the informational content of a bankruptcy flag received 7–10 years ago is relatively less important for employers than an individual’s more recent delinquencies. Finally, Balance, Clifford, and Shoag (2016), Bartik and Nelson (2016), and Cortes, Glover, and Tasci (2016) study equilibrium effects in the labor markets of bans imposed by U.S. states on the use of credit information on hiring decisions. Our work also speaks to several strands of household finance research. First, we contribute to the literature on the impacts of credit market information on credit market outcomes.11 Second, we add to previous work that studies the effects of debt renegotiation on households.12 Third, our paper is relevant for the literature on the interaction between entrepreneurship and credit supply (e.g., see the citations in footnote 6). Our findings also speak to the current academic and policy debates surrounding the appropriate scope of use for credit information by employers, in particular in the context of the increasing use of large data sets in economic decisions, that is, “big data” (e.g., see Einav and Levin 2014).13 1. Measuring the Employment Cost of Default 1.1 Setting and policy change 1.1.1 Swedish credit registries and policy change Credit registries are repositories of information on the past repayment of debts and other claims, such as utility bills, credit cards, and mortgage payments. In Sweden, credit registries collect registered data from 3 main sources: the national enforcement agency (Kronofogden), the tax authorities, and the Swedish banking sector.14 Each reported default triggers an arrear on the borrower’s credit report. In Sweden, any person or company can in principle buy and view the credit records of any other individual.15 Financial institutions that report to the registry are able to view the entire credit file, including the summary credit score and number of arrears, while noncontributing institutions and private people are only shown a strict subset of the recorded information. Noncontributing entities observe neither the credit score nor the number of arrears. They instead see a nonpayment flag, which indicates at least one arrear. Before October 2003, Swedish law mandated that all arrears be removed from each individual’s credit report 3 years after the nonpayment occurred. In practice, the credit registries removed all arrears on December 31 of the third year after the nonpayment occurred. Beginning in October 2003, the Swedish government changed the interpretation of the law to remove every past arrear from the credit registries exactly 3 years after the nonpayment was recorded.16 Notably for identification, the change was motivated by an upgrade to the registries’ IT capabilities and not by changes to the type or frequency of defaulters. As shown in Figure 1, the adjustment to the law induced a sharp change in the time series pattern of arrear removals by the credit registries. The figure plots the bimonthly number of people with arrears that were no longer reported in the credit registry. The figure shows that before 2003, arrears were almost only removed from the credit registry on the last day of the year.17 Further, the figure shows a noticeable spike in the frequency of removals in October 2003. This spike corresponds to the removal of the stock of arrears that had occurred between January and the end of September 2000 and that had not yet been deleted from the credit registry. After October 2003, the frequency is more smoothly distributed over the year, in effect following the distribution of nonpayments across the year, 3 years earlier. Figure 1 View largeDownload slide Frequency of removal of nonpayment flag over time This figure displays the distribution of the removal of nonpayments over time. In the Old regime the credit registry removed all eligible arrears once a year, on December 31. Because of the bimonthly feature of our data, and because removals are inferred as differences in the stock of reported defaults, these nonpayments corresponds to the February–March bimonth (labeled February). This regime ended at the end of September 2003, when the law change came into effect and the credit registry removed arrears exactly 3 years to the day after the default was first reported. Figure 1 View largeDownload slide Frequency of removal of nonpayment flag over time This figure displays the distribution of the removal of nonpayments over time. In the Old regime the credit registry removed all eligible arrears once a year, on December 31. Because of the bimonthly feature of our data, and because removals are inferred as differences in the stock of reported defaults, these nonpayments corresponds to the February–March bimonth (labeled February). This regime ended at the end of September 2003, when the law change came into effect and the credit registry removed arrears exactly 3 years to the day after the default was first reported. 1.1.2 Identification intuition We attempt to identify the causal effects of past nonpayment information on employment and other labor market outcomes. A simple correlation between credit information and employment would likely be plagued by both reverse causality and omitted variable bias.18 Rather, an idealized experiment to identify this causal effect would consider two identical groups of people who defaulted in the past and subsequently repaid but, as a result, have a bad credit record. In that experiment, the credit registry would delete the information for one group earlier than scheduled and any difference in the employment of both groups could be causally assigned to the removal of information. In our empirical setting, we use the variation in the retention time of publicly observable arrears induced by the 2003 policy change in Sweden to approximate this idealized setting. One naive empirical strategy would be to focus on nonpayment cohorts before the policy change and to compare people who defaulted earlier in the year to those who defaulted later in the year. After all, the early defaulters did experience longer retention times than the end-of-year defaulters. However, it is likely that people who default at different times during the year differ in ways that may have systematically different labor market outcomes.19 Further, people may have been aware of the pattern of deletions and chose to time their defaults accordingly if possible. Hence, a comparison of the employment prospects of people who defaulted early and late in the same year before the policy change is likely to be biased. An alternative identification strategy is to compare people who defaulted in 2000, which we define as the “Old regime,” with those who defaulted in 2001, which we define as the “New regime,” observing that the average retention time is lower for the New regime. Indeed, the policy change induced unexpected variation in the length of time that information was retained in the credit registries. Hence, people who defaulted in 2000, 3 years prior to the policy change, did so under the same beliefs about retention time as people who defaulted in 2001, 2 years before the policy change. The unexpected nature of the policy change allows us to rule out any strategic behavior of people timing their default so as to experience shorter retention times. However, this strategy is also problematic as there may be other differences between people who defaulted in 2000 or in 2001 that are correlated with labor market outcomes. Instead, we combine the two empirical strategies—New versus Old regime cohorts and early versus late defaulters within the calendar year—for identification. We compare the difference in the employment prospects of people in the New regime whose default was reported early and late in the year with the same difference for people in the Old regime. We observe that people in the New regime who defaulted at any point in 2001 and people in the Old regime who defaulted late in 2000 were subject to the same 3-year retention times. People in the Old regime group who defaulted early in 2000 were subject to more than 3 years of retention time. For example, people in the Old regime group who defaulted in March 1 were subject to 3 years and 7 months of retention time. This double-difference analysis is the basis of our identification strategy. We then compare the employment outcomes for each individual before and after the 3-year post-arrear date. The identification assumption we make is that, in the absence of the policy change, the difference in employment outcomes of people in the Old and New regimes whose defaults were reported early and late in the year would have remained constant before and after the deletion of the nonpayment flag. In Section 2.1 we provide pre-trends evidence that is consistent with this assumption. Finally, among people in the New regime, those who defaulted earlier in the year experienced a larger decrease in retention time than those who defaulted later in the year. This suggests an additional test of our identification strategy: the effects of the policy change should be monotonically decreasing in the time of the year during which defaults were initially reported. In Section 2 we provide evidence that is consistent with this intuition. 1.2 Data Our initial sample comprises the near universe of alternative credit borrowers in Sweden. This sample was generously supplied by the Swedish pawnbroker industry and contains registered information about the 332,351 people who took out at least one pawn loan between 1999 and 2012 (approximately 5% of the Swedish adult population). It is true that people who resort to pawn borrowing are systematically different from the Swedish population at large. Given that people typically turn to pawn loans when they are not able to access sufficient credit from formal sources to meet their demand, unsurprisingly, pawn borrowers tend to be poorer, are less likely to be employed, earn lower wages conditional on being employed, and are less likely to be homeowners (Bos, Carter, and Skiba 2012).20 To paint a more complete picture of the population of Swedish pawn borrowers, we plot for the years of our sample the age, education, income and credit score distribution, and compare it to the distributions of the Swedish population at large (see the Internet Appendix). From these plots we learn that, on average, the Swedish pawn borrower is younger, less educated, earns a lower income, and has a worse credit score (a higher probability of default) compared to the average Swede. Importantly, the policy we study only matters for the potential outcomes of people with arrears. So, it is useful to ask what fraction of total defaulters in Sweden is represented in our sample. While the average Swede has a 10% likelihood of having at least one arrear, the number is 46% in our sample. This implies that we have data on approximately one quarter of arrear-holders in the country. Given the poor financial records and weak attachment to the labor market of alternative borrowers, it is exactly this population that may experience the greatest benefits from a clean credit record. We obtain a bimonthly panel of credit data from the leading Swedish credit registry, Upplysningscentralen that ranges from 2000 to 2005. Each bimonthly observation contains a snapshot of the individual’s full credit report (i.e., amount of credit and repayment status on different obligations). Swedish credit registries also have access to data from the Swedish Tax authority and other agencies. This enables us to further observe variables such as home ownership, age, marital status, yearly income from work, and self-employment. Importantly, we observe when an individual’s nonpayment was first reported and subsequently removed by the credit registry. To measure labor market outcomes, we match the credit registry data with information obtained from Statistics Sweden (SCB). These data are at the yearly level from 2000 to 2005 and include information on each individual’s employment status. The data also include measures of individual income, wages, and income from self-employment plus total household disposable income. We defer an analysis of summary statistics of our main outcome variables until after we have presented our sample selection criteria. 1.3 Implementation of empirical strategy The key empirical goal of the paper is to understand what happens when the defaulter flag is removed exogenously from the top of the credit report. The natural experiment in the paper allows us a unique opportunity to use quasi-exogenous variation to measure this impact. However, as in any heterogeneous treatment effects setting, the experiment doesn’t impact all households equally. For example, households with no arrears (the always-takers) and households who continue receiving arrears even after the policy announcement (the never takers) should not be affected directly. Thus, we make a series of sample restrictions to attempt to isolate people who, ex ante, are most likely to be affected by the policy (the compliers). First, we include in our analysis sample only people who received an arrear for nonpayment in 2000 or in 2001 and thus had those nonpayment flags removed in 2003 or 2004. Second, we further restrict the sample to people who did not receive additional arrears in the subsequent 20 months (i.e., who repaid all their delinquencies) before the policy change. This restriction reduces the sample size by 67% (i.e., 33% of all people in our sample who had an arrear in 2000 or 2001 did not redefault in the next 20 months). The rationale for this 20-month window is as follows. Recall that our identification strategy requires categorizing people into New and Old cohorts. With a shorter than 20-month window, it becomes unclear whether an individual who recorded an arrear in March 2000 and another in October 2001 should be in the Old or New regime. It is also essential that our sample construction be predetermined relative to the policy change. Thus, a longer than 20-month window would be contaminated by the endogenous choice of redefault caused by the policy change.21 Third, because of the bimonthly nature of the credit registry data shared with the researchers (e.g., December–January defaulters are first reported in the February snapshot, February–March in the April snapshot, and so on), we restrict our sample to defaults occurring strictly after January 2000.22 For a similar reason we omit people whose defaults are removed from the credit registry in the December-January 2001 bimonth. Finally, we focus on people who are between 18 and 75 years old the year before information on past defaults is removed from the credit registry. These selection criteria, which are necessary to implement our empirical strategy, result in a sample of 15,232 people. Figure 2 depicts the time line of the policy change and how it affected the length of time in which nonpayments were reported for the people in our sample. In particular, nonpayments of people in the Old regime were recorded in the first months of the year were reported in the credit registries for a maximum of almost 3 years and 8 months until the end of September 2003, while nonpayments of people in the New regime were recorded in the first months of the year were reported in the credit registries for exactly 3 years. Figure 2 also shows the number of past defaulters in each of the bimonthly bins. Although there are substantially more early defaulters than late defaulters in both cohorts, these patterns are remarkably consistent across New and Old regimes. Figure 2 View largeDownload slide Time line This figure depicts the time line of the policy change that enforced a 3-year retention time for reporting defaults and how this policy generated variation in the retention time of the nonpayment flag. In particular, people whose nonpayment occurred early in 2001 had a reduced retention time of past nonpayments. In contrast, people whose nonpayment occurred early in 2000 were reported in the credit registries until October 2003. Figure 2 View largeDownload slide Time line This figure depicts the time line of the policy change that enforced a 3-year retention time for reporting defaults and how this policy generated variation in the retention time of the nonpayment flag. In particular, people whose nonpayment occurred early in 2001 had a reduced retention time of past nonpayments. In contrast, people whose nonpayment occurred early in 2000 were reported in the credit registries until October 2003. Table 1 reports the excess number of months above 3 years that the nonpayment flag of people in each of the four cells – New regime-Early, New regime-Late, Old regime-Early and Old regime-Late – is retained in the credit registry after the policy change. All people in the New regime have a retention time of 3 years (reported in the table as zero excess months above 3 years). Old regime people who defaulted early in the year have on average 6 extra months of retention time, calculated as follows: February defaulters have on average 7.5 extra months of retention time of their nonpayment flag – from any day in February to the first day of October – March defaulters have 6.5 extra months, April defaulters have 5.5 extra months, and May defaulters have 4.5 extra months. Assuming a uniform distribution of people across all 4 months results in an average extra retention time of 6 months. Finally, Old regime people who defaulted late in the year have 1 extra month of retention time (calculated as: August defaulters have 1.5 extra months, September defaulters have 0.5 extra months, and October and November defaulters have exactly 3 years of retention time given that the policy change occurred precisely on the first day of October). Table 1 Average retention months Early Late New regime 0 0 Old regime 6 0.5 Early Late New regime 0 0 Old regime 6 0.5 Average retention months of the nonpayment flag in the credit registry in excess of 3 years are shown for the New and Old regimes, who defaulted early (February–May) or late (August–November). Table 1 Average retention months Early Late New regime 0 0 Old regime 6 0.5 Early Late New regime 0 0 Old regime 6 0.5 Average retention months of the nonpayment flag in the credit registry in excess of 3 years are shown for the New and Old regimes, who defaulted early (February–May) or late (August–November). We define the indicator variable $$New_{i}$$ to equal one if borrower $$i$$’s last nonpayment occurred during 2001 and zero if it occurred during 2000. We interact $$New_{i}$$ with the dummy variable $$Early_{i}$$, which distinguishes between people whose nonpayments occurred early and late during the year. Because in our data each individual is assigned to a bimonthly cohort of defaulters, $$Early_{i}$$ equals one for people whose last nonpayment occurred in the February-March or April-May bimonths, and zero for people whose last nonpayment occurred in the August–September or October–November bimonths.23 Finally, we create a dummy, $$Post_{i,t}$$, which equals one for all event years after borrower $$i$$’s nonpayment signal is removed (2003 for the Old regime and 2004 for the New regime). The variable $$Post_{i,t}$$ is measured in event time $$t$$, which is normalized to zero in 2000 for the Old regime and in 2001 for the New regime. Thus, event time year 3 represents the year in which the nonpayment flag is deleted from the credit registry for any individual in our sample. Our main specification is the following reduced-form model: \begin{align} Employed_{i,t} & = \omega_{i}+\omega_{t}+\omega_{\tau}+\beta New_{i}\times Early_{i}\times Post_{i,t}+\delta Post_{i,t}\nonumber \\ & \quad + \gamma New_{i}\times Post_{i,t}+\lambda Early_{i}\times Post_{i,t}+\varepsilon_{i,t}.\label{eq:regression} \end{align} (1) We include individual fixed effects $$\omega_{i}$$, calendar year fixed effects $$\omega_{\tau}$$, and event time fixed effects $$\omega_{t}$$, as well as all double interactions that are not absorbed by fixed effects. For completeness, we present in the Internet Appendix selected Swedish macroeconomic indicators throughout our sample period.24 The table suggests that although there is some volatility in economic aggregates, no major recessions were observed in Sweden during this time period. In particular, gross domestic product (GDP) growth dropped from 4.7% in 2000 to 1.6% in 2001, although unemployment dropped from 5.8% to 5% in the same time frame. Inflation is relatively constant and below 2.41%, and unemployment varied between 5% and 8% throughout the sample period. The variable $$\omega_{i}$$ absorbs the baseline and interaction coefficients of $$New_{i}$$ and $$Early_{i}$$. The coefficient $$\beta$$, our key parameter of interest, measures the differential probability of being employed for the New and Old regimes, for people whose nonpayment was reported early in the year relative to those whose nonpayment was reported late in the year, the year(s) after each individual’s nonpayment is no longer reported relative to the 3 prior years. The coefficients $$\delta$$ and $$\lambda$$ capture differences in employment for people in the Old regime whose nonpayment occurred late and early in the year, respectively, the years after the arrear is deleted. Finally, $$\gamma$$ captures differential employment trends for all people in the New regime after their nonpayment information is no longer publicly available. 1.4 Summary statistics Before presenting the regression results, we present the definitions of our dependent variables in Table 2 and selected summary statistics in Table 3. We focus our analysis on employment outcomes, broadly construed. In addition to earnings and whether an individual has a job, we also consider alternatives to labor income, including seeking more education and turning to self-employment income. The top panel presents a brief definition for each of our outcome variables, and the lower panel displays selected sample statistics. Table 2 Definitions of dependent variables Employed A dummy that equals one if the individual is employed conditional on being in labor force 1(Wages$$>0$$) A dummy that equals one if the individual has positive income from work log(Income + 1) Logarithm of yearly post-tax income, in 100 SEK; zeros replaced by 1 log(Wages + 1) Logarithm of yearly pre-tax income from work, in 100 of SEK; zeros replaced by 1 Self-employed A dummy that equals one if the individual received positive wages from entrepreneurship Relocates A dummy that equals one if individual’s residence is in a different county from previous year Years of schooling Number of years of completed education, inferred from end of year level of education Financial inquiries Number of requests for an individuals’ credit report by financial institutions Nonfinancial inquiries Number of requests for an individuals’ credit report by nonfinancial institutions Employed A dummy that equals one if the individual is employed conditional on being in labor force 1(Wages$$>0$$) A dummy that equals one if the individual has positive income from work log(Income + 1) Logarithm of yearly post-tax income, in 100 SEK; zeros replaced by 1 log(Wages + 1) Logarithm of yearly pre-tax income from work, in 100 of SEK; zeros replaced by 1 Self-employed A dummy that equals one if the individual received positive wages from entrepreneurship Relocates A dummy that equals one if individual’s residence is in a different county from previous year Years of schooling Number of years of completed education, inferred from end of year level of education Financial inquiries Number of requests for an individuals’ credit report by financial institutions Nonfinancial inquiries Number of requests for an individuals’ credit report by nonfinancial institutions Table 2 Definitions of dependent variables Employed A dummy that equals one if the individual is employed conditional on being in labor force 1(Wages$$>0$$) A dummy that equals one if the individual has positive income from work log(Income + 1) Logarithm of yearly post-tax income, in 100 SEK; zeros replaced by 1 log(Wages + 1) Logarithm of yearly pre-tax income from work, in 100 of SEK; zeros replaced by 1 Self-employed A dummy that equals one if the individual received positive wages from entrepreneurship Relocates A dummy that equals one if individual’s residence is in a different county from previous year Years of schooling Number of years of completed education, inferred from end of year level of education Financial inquiries Number of requests for an individuals’ credit report by financial institutions Nonfinancial inquiries Number of requests for an individuals’ credit report by nonfinancial institutions Employed A dummy that equals one if the individual is employed conditional on being in labor force 1(Wages$$>0$$) A dummy that equals one if the individual has positive income from work log(Income + 1) Logarithm of yearly post-tax income, in 100 SEK; zeros replaced by 1 log(Wages + 1) Logarithm of yearly pre-tax income from work, in 100 of SEK; zeros replaced by 1 Self-employed A dummy that equals one if the individual received positive wages from entrepreneurship Relocates A dummy that equals one if individual’s residence is in a different county from previous year Years of schooling Number of years of completed education, inferred from end of year level of education Financial inquiries Number of requests for an individuals’ credit report by financial institutions Nonfinancial inquiries Number of requests for an individuals’ credit report by nonfinancial institutions Table 3 Summary statistics Mean SD Median Dependent variables (1) (2) (3) Employed 0.43 0.50 1(Wages$$> 0$$) 0.79 0.40 log(Income + 1) 5.62 2.91 7.03 Income 914 719 913 log(Wages + 1) 5.57 2.97 7.04 Wages 1,184 1,070 1,134 Self-employed 0.05 0.21 Relocates 0.07 0.27 Years of schooling 10.70 1.76 11 Financial inquiries 0.52 1.05 Nonfinancial inquiries 0.54 0.95 Age 42.83 13.00 42 Male 0.60 0.49 Home owner 0.09 0.29 Number of people 15,232 Mean SD Median Dependent variables (1) (2) (3) Employed 0.43 0.50 1(Wages$$> 0$$) 0.79 0.40 log(Income + 1) 5.62 2.91 7.03 Income 914 719 913 log(Wages + 1) 5.57 2.97 7.04 Wages 1,184 1,070 1,134 Self-employed 0.05 0.21 Relocates 0.07 0.27 Years of schooling 10.70 1.76 11 Financial inquiries 0.52 1.05 Nonfinancial inquiries 0.54 0.95 Age 42.83 13.00 42 Male 0.60 0.49 Home owner 0.09 0.29 Number of people 15,232 Panel A defines the dependent variables. Panel B presents sample statistics for the 3 years before flag deletion, including 2000, 2001, and 2002 for the New regime and 2001, 2002, and 2003 for the Old regime. Table 3 Summary statistics Mean SD Median Dependent variables (1) (2) (3) Employed 0.43 0.50 1(Wages$$> 0$$) 0.79 0.40 log(Income + 1) 5.62 2.91 7.03 Income 914 719 913 log(Wages + 1) 5.57 2.97 7.04 Wages 1,184 1,070 1,134 Self-employed 0.05 0.21 Relocates 0.07 0.27 Years of schooling 10.70 1.76 11 Financial inquiries 0.52 1.05 Nonfinancial inquiries 0.54 0.95 Age 42.83 13.00 42 Male 0.60 0.49 Home owner 0.09 0.29 Number of people 15,232 Mean SD Median Dependent variables (1) (2) (3) Employed 0.43 0.50 1(Wages$$> 0$$) 0.79 0.40 log(Income + 1) 5.62 2.91 7.03 Income 914 719 913 log(Wages + 1) 5.57 2.97 7.04 Wages 1,184 1,070 1,134 Self-employed 0.05 0.21 Relocates 0.07 0.27 Years of schooling 10.70 1.76 11 Financial inquiries 0.52 1.05 Nonfinancial inquiries 0.54 0.95 Age 42.83 13.00 42 Male 0.60 0.49 Home owner 0.09 0.29 Number of people 15,232 Panel A defines the dependent variables. Panel B presents sample statistics for the 3 years before flag deletion, including 2000, 2001, and 2002 for the New regime and 2001, 2002, and 2003 for the Old regime. Our summary stats are estimated on the 3 years before nonpayment flags are removed, which correspond to the years 2000, 2001, and 2002 for the Old regime and 2001, 2002, and 2003 for the New regime. Our main outcome variables are Employed, a dummy that equals one for people who were continuously employed throughout the year, and $$1\left(Wages>0\right)$$, a dummy that equals one if the individual received any wage income during the year. During those years, an average of 43% of people in our sample are employed during the full year, whereas 79% received some positive wage income. We view the discrepancy between both averages as consistent with two particular facts about our sample. First, people in our sample have much higher job instability than the average Swede, in part because of their lower levels of education. As a result, an individual in our sample is more likely to receive some positive income from wages and at the same time experience unemployment spells during the year, thus being categorized as not fully employed as per our main outcome variable. Second, because of their lower education, people in our sample are more likely to have temporary, low-skill employment contracts. We verify this notion using aggregate data from Statistics Sweden on the relationship between education levels and labor market contracts for the general Swedish population. We see that 14.1% of the employment of people who drop out of high school is temporary, while this figure drops to 10% for people with more than a high school eduation.25 Average after-tax income is equal to SEK91,400 (approximately $${\$}$$12,000). We use a log transformation of our income measures, which are in units of hundreds of Swedish Kronor (SEK), as the outcome variable in our regression tests, and average log(Income+1) is 5.6. Roughly 5% of all people in our sample are self-employed. Finally, people are 42.8 years old on average and 60% male. The low rates of formal employment and average wage earnings confirm that our sample is indeed situated at the margins of formality, where negative credit information could lead to costly labor market exclusion. For comparability, we present in in the Internet Appendix selected summary stats obtained from the credit registry for a random sample of the Swedish population and for a random sample of people with at least one arrear, both as of 2003. The average probability of having any wage income in our analysis sample is closer to the sample that represents all Swedish defaulters (79% in our sample versus 86% for the random sample conditional on default). Moreover, based on our calculations, the average income in our sample corresponds roughly to the 10th percentile of the income distribution in Sweden as of 2003, while the average income for the Swedish sample conditional on any arrear is at the 13th percentile that same year. One limitation of the data is that it does not include information on the individual’s job or industry. To provide additional context for our sample, we obtain from Statistics Sweden information on the most common jobs categorized by education levels during our sample period. For people with 9 to 12 years of education, common jobs include; caretaker in the health care sector, retail salesperson, finance and sales associate, truck driver, construction worker, and janitor.26 Several of these industries, such as financial services, transportation, retail, and construction, report to check credit records for their applicants.27 2. Results 2.1 Graphical evidence We start by showing graphically the event-time evolution of the average outcomes, which provides evidence in support of our identification assumption. The identification assumption for regression (1) is that, in the absence of the policy change, the probability of being employed for the New and Old regimes would have evolved in parallel between early and late in the year defaulters. We provide evidence that supports this assumption in Figure 3. The top panel shows the average of $$Employed$$ (we omit subindeces for brevity), defined as a dummy for whether the individual was fully employed throughout the entire year, as well as $$1(Wages>0)$$, the average of a dummy that equals one for people who receive any positive wage during the year. The x-axis shows event time years, which are defined starting at zero in 2000 for the Old regime and in 2001 for the New regime. We look for parallel trends in the preperiod, and indeed, there are no detectable differences in the trends of the difference of either variable between early and late defaulters in the New and Old regimes during the 3 years before removal of the nonpayment flag (i.e., in event times 0 to 2).28 Similar effects can be observed for the average log income and log wage income, where zeros have been replaced by ones, shown in the lower panel. These graphs provide evidence that is consistent with our identification assumption. Below we also provide a formal test of (absence of) pretrends using lagged outcomes in a regression setting. Figure 3 View largeDownload slide Pre-trends This figure shows that there is no difference in the preperiod trends (before the policy change) of the difference between Early and Late defaulters, in the New regime and in the Old regime for our main outcomes. The top panel shows preperiod trends for $$employed$$ and $$1(Wages>0)$$, which equals one if an individual received any wage income, and the lower panel shows the same for $$\log(Wages+1)$$ and $$\log(Income+1)$$, where zeros have been replaced by 1. The solid lines represent the differences in averages of the respective outcome variables between people who defaulted early in the year (high exposure) and people who defaulted late in the year (low exposure), for people in the Old regime. The dashed line represents the same difference for people in the New regime group. Figure 3 View largeDownload slide Pre-trends This figure shows that there is no difference in the preperiod trends (before the policy change) of the difference between Early and Late defaulters, in the New regime and in the Old regime for our main outcomes. The top panel shows preperiod trends for $$employed$$ and $$1(Wages>0)$$, which equals one if an individual received any wage income, and the lower panel shows the same for $$\log(Wages+1)$$ and $$\log(Income+1)$$, where zeros have been replaced by 1. The solid lines represent the differences in averages of the respective outcome variables between people who defaulted early in the year (high exposure) and people who defaulted late in the year (low exposure), for people in the Old regime. The dashed line represents the same difference for people in the New regime group. The figures also hint at our main results: people in the New regime who default early in the year exhibit a higher probability of employment and earn higher incomes after their nonpayment flags are removed relative to similar people in the Old regime. In general, the graphs show that the difference in employment outcomes between early and late defaulters is positive but decreasing over time for both cohorts, but, in event time 3, that difference shrinks less for New regime. This suggests that the effect is driven by a relatively lower probability of employment for people in the Old regime who default early in the year, which is consistent with the credit information mechanism. For these people, the past nonpayment flag remains in the credit records for an extra 6 months (above 3 years), relative to half an extra month of retention time for Old regime people who defaulted late and no extra months for people in the New regime, as is shown in Table 1. 2.2 Main results Table 4 presents the output of regression (1). Columns 1, 2, and 3 present the regression results when the outcome is Employed. Column 1 documents that the probability of employment for an individual whose information is reported for a shorter period increases by 2.8 percentage points the year the nonpayment is removed from the registry (year 3). This effect is a 6.5% increase relative to the preperiod average employment rate (43%).29 Column 2 shows that this effect is also significant for the combined 2 years after removal, although with a lower magnitude. Column 3 shows that focusing only on the second year after removal, the point estimate continues to be positive, although statistical significance is lost. Table 4 Employment outcomes Employed Employed Employed $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0280** 0.0203* 0.0125 0.0298** 0.0299*** 0.0295** (0.013) (0.012) (0.014) (0.012) (0.011) (0.014) Post-period (years) 1 2 Only 2 1 2 Only 2 Obs 50,623 63,113 50,482 50,623 63,113 50,482 $$R^{2}$$ 0.002 0.003 0.003 0.007 0.024 0.027 No. of people 12,664 12,664 12,664 12,664 12,664 12,664 Employed Employed Employed $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0280** 0.0203* 0.0125 0.0298** 0.0299*** 0.0295** (0.013) (0.012) (0.014) (0.012) (0.011) (0.014) Post-period (years) 1 2 Only 2 1 2 Only 2 Obs 50,623 63,113 50,482 50,623 63,113 50,482 $$R^{2}$$ 0.002 0.003 0.003 0.007 0.024 0.027 No. of people 12,664 12,664 12,664 12,664 12,664 12,664 This table shows that public information on past defaults causally reduces employment. The table shows the coefficient $$\beta$$ from regression: \begin{align*} Employed_{i,t}&= \alpha_{i}+\omega_{t}+\nu_\tau + \beta Early_i\times New_{i}\times Post_{i,t}+\delta Post_{i,t}\\ &\quad +\gamma New_{i}\times Post_{i,t}+\lambda Early_{i}\times Post_{i,t}+\varepsilon_{i,t}. \end{align*} Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 4 Employment outcomes Employed Employed Employed $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0280** 0.0203* 0.0125 0.0298** 0.0299*** 0.0295** (0.013) (0.012) (0.014) (0.012) (0.011) (0.014) Post-period (years) 1 2 Only 2 1 2 Only 2 Obs 50,623 63,113 50,482 50,623 63,113 50,482 $$R^{2}$$ 0.002 0.003 0.003 0.007 0.024 0.027 No. of people 12,664 12,664 12,664 12,664 12,664 12,664 Employed Employed Employed $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0280** 0.0203* 0.0125 0.0298** 0.0299*** 0.0295** (0.013) (0.012) (0.014) (0.012) (0.011) (0.014) Post-period (years) 1 2 Only 2 1 2 Only 2 Obs 50,623 63,113 50,482 50,623 63,113 50,482 $$R^{2}$$ 0.002 0.003 0.003 0.007 0.024 0.027 No. of people 12,664 12,664 12,664 12,664 12,664 12,664 This table shows that public information on past defaults causally reduces employment. The table shows the coefficient $$\beta$$ from regression: \begin{align*} Employed_{i,t}&= \alpha_{i}+\omega_{t}+\nu_\tau + \beta Early_i\times New_{i}\times Post_{i,t}+\delta Post_{i,t}\\ &\quad +\gamma New_{i}\times Post_{i,t}+\lambda Early_{i}\times Post_{i,t}+\varepsilon_{i,t}. \end{align*} Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Columns 4, 5, and 6 in Table 4 show the same pattern when employment is defined instead as receiving any positive labor market income during the year. Indeed, Column 4 shows that people in the New regime who defaulted early in the year are 3 percentage points more likely to earn positive labor income, and this effect persists 2 years post-information removal. Furthermore, the probability of receiving positive income from work is positive (and statistically significantly so) and of the same magnitude during the second year (Column 6). The persistence of these effects suggests that default induces a longer-term cost in the labor market, which is consistent with the findings in the labor economics literature that a longer unemployment spell has a persistent effect on future unemployment (e.g., Kroft, Lange, and Notowidigdo 2013).30 In the Internet Appendix, we present regression results using our main specification (i.e., regression (1)), where the outcome variables are lagged by 1 year. These regressions measure effects 1 year before the information is removed, and are akin to a test of pre-trends in a standard difference-in-differences specification. In all cases, the coefficient of interest is not detectably different from zero, formalizing the lack of visible pre-trends in Figure 3 and providing further support to our identification assumption. We explore the impact of credit market information on additional labor market outcomes. Columns 1 to 3 in Table 5 display the output of our main regression model (1), where the postperiod corresponds to 2 years after the removal of the nonpayment flag, for an array of additional labor market outcomes including the log of income from work, log(Wages + 1), the probability of being self-employed, and the log of total post-tax income, log(Income + 1). Income measures are in hundreds of SEK.31 In Column 1 we find that people whose nonpayment flag was retained for less time earn statistically significantly higher wage incomes. Table 5 Wages, income, and self-employment log(Wages + 1) Self employed log(Income + 1) Coefficient (1) (2) (3) $$\beta$$ 0.1995*** –0.0137** 0.1410* (0.077) (0.005) (0.075) Post-period (years) 2 2 2 Obs 63,113 63,113 63,113 $$R^{2}$$ 0.030 0.003 0.040 People 12,664 12,664 12,664 log(Wages + 1) Self employed log(Income + 1) Coefficient (1) (2) (3) $$\beta$$ 0.1995*** –0.0137** 0.1410* (0.077) (0.005) (0.075) Post-period (years) 2 2 2 Obs 63,113 63,113 63,113 $$R^{2}$$ 0.030 0.003 0.040 People 12,664 12,664 12,664 This table shows the effects of credit information on (log)wage income, self-employment, and (log)income, using our main regression model: \begin{align*} Outcome_{i,t}&= \alpha_{i}+\omega_{t}+\nu_\tau + \beta Early_i\times New_{i}\times Post_{i,t}+\delta Post_{i,t}\\ &\quad +\gamma New_{i}\times Post_{i,t}+\lambda Early_{i}\times Post_{i,t}+\varepsilon_{i,t}. \end{align*} Zeros are replaced by 1 in the log outcomes. Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 5 Wages, income, and self-employment log(Wages + 1) Self employed log(Income + 1) Coefficient (1) (2) (3) $$\beta$$ 0.1995*** –0.0137** 0.1410* (0.077) (0.005) (0.075) Post-period (years) 2 2 2 Obs 63,113 63,113 63,113 $$R^{2}$$ 0.030 0.003 0.040 People 12,664 12,664 12,664 log(Wages + 1) Self employed log(Income + 1) Coefficient (1) (2) (3) $$\beta$$ 0.1995*** –0.0137** 0.1410* (0.077) (0.005) (0.075) Post-period (years) 2 2 2 Obs 63,113 63,113 63,113 $$R^{2}$$ 0.030 0.003 0.040 People 12,664 12,664 12,664 This table shows the effects of credit information on (log)wage income, self-employment, and (log)income, using our main regression model: \begin{align*} Outcome_{i,t}&= \alpha_{i}+\omega_{t}+\nu_\tau + \beta Early_i\times New_{i}\times Post_{i,t}+\delta Post_{i,t}\\ &\quad +\gamma New_{i}\times Post_{i,t}+\lambda Early_{i}\times Post_{i,t}+\varepsilon_{i,t}. \end{align*} Zeros are replaced by 1 in the log outcomes. Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. But how large is this earnings effect? In the Internet Appendix we show that running our our main regression in wage levels implies an increase in wages of 3,987 SEK, or roughly $${\$}$$480. Recall from Table 1 that this $${\$}$$480 treatment effect is the result of a reduction in retention time of only 5.5 months. Thus, this cost annualizes to $${\$}$$1,047 per year or $${\$}$$3,142 over the 3 years in which default is flagged publicly. This effect is economically large, approximately 7% of the average annual earnings for people in our sample.32 Recall that improved credit information may also directly increase the amount of credit financial institutions are willing to supply. To get a sense of the relative magnitudes of the earnings and credit supply effects, in the Internet Appendix, we run our main regression using credit outcomes, specifically, the amount of consumer credit and a dummy for any positive consumer credit. We find that the removal of the nonpayment flag leads to an increase in credit of 903 SEK (Column 2), which implies a total annualized effect of $${\$}$$236 in credit per extra year of retention time.33 Thus, the effect of credit information on wages is roughly four times the effect on credit, and suggests that, quantitatively, the labor costs of default may be more important than the loss of access to credit, at least among people at the margins of formality. The wage earnings effect combines the extensive margin effect documented above with an intensive margin effect of higher salaries conditional on employment. We estimate in a back-of-the-envelope calculation that approximately 53% of the earnings effect is driven by the extensive margin.34 These calculations imply important effects on both intensive and extensive margins, which is consistent with the existence of labor market frictions that prevent an adjustment on wages alone.35 In addition to wages, people may also earn incomes from self-employment activities. Column 2 in Table 5 shows that shortened retention times lead to a decrease in self-employment activities. This decrease is despite an increase in the availability of credit, which suggests that many people in our sample use self-employment as a response to unemployment rather than as a high-growth venture.36 Summing across the increase in wage earnings and the decrease in self-employment income, we find an overall increase in post-tax income in Column 3 in Table 5. As an additional robustness test, in the Internet Appendix, we present the results of running our main regression test on a sample where we shift the definition of New and Old regimes 1 year ahead. That is, we define a Placebo New regime as people who defaulted in 2001 and a Placebo Old regime as people who defaulted in 2002, and use $$Employed$$, a dummy for positive wage income, and the log of wages plus one as outcomes. In all 3 cases, the estimated coefficient of interest is not significantly different from zero at conventional levels and even takes the opposite sign to our main results, which supports the assumption that our main results are not driven by differential secular employment trends of defaulters. 2.3 Results by treatment intensity Our identification strategy relies on variation in the retention times of nonpayment information induced by the policy change. To further support our identification, we exploit the bimonthly nature of our credit data and study whether people who were exposed to differential retention times, measured by the time of the year in which they defaulted, experience differential labor market responses. We categorize people in our sample into five groups according to the bimonth in which they defaulted: February–March, April–May, June–July, August–September, and October–November.37 This categorization of default cohorts induces a monotonic ordering of exposure to the policy change, defined as the average reduction in the number of months during which the nonpayment flag was available in the credit registry, for people in the New regime relative to Old regime: the August–September cohort has a 1-month average reduction, June–July has a 3-month average reduction, April–May has a 5-month average reduction, and February–March has a 7-month average reduction. The October–November cohort has, by construction, a 0-month reduction in retention time. We hypothesize that if past arrears affect the probability of being employed, then the measure of months of exposure to the policy, i.e. the number of fewer months in which past arrears are reported, should be positively correlated with the probability of being employed during a given year. To test this hypothesis, we present in Table 6 the results of a regression where we allow the effect of a shorter retention time of past defaults to be linear in the length of exposure, $$Exposuremonths_{i}$$, defined as the reduction in the retention time for the New cohort relative to the Old cohort (i.e., by bimonth of default). \begin{align} 1\left(Wages>0\right){}_{i,t} & =\, \omega_{i} + \omega_{t} + \omega_{\tau} \nonumber \\ &\quad + \beta Exposuremonths_{i}\times New_{i}\times Post_{i,t} \nonumber \\ &\quad + \delta Post_{i,t} + \gamma New_{i}\times Post_{i,t} \nonumber \\ &\quad + \sum_{\tau=1,3,5,7}\lambda_{\tau}1\left(Exposuremonths_{i}=\tau\right)\times Post_{i,\tau} \nonumber \\ &\quad + \varepsilon_{i,t}.\label{eq:linear_effects} \end{align} (2) Table 6 Employment outcomes with varying treatment intensity $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ log(Wages + 1) log(Wages + 1) Coefficient (1) (2) (3) (4) $$\beta$$ 0.0051** 0.0059*** 0.0364*** 0.0398*** (0.002) (0.002) (0.013) (0.013) Post-period (years) 1 2 1 2 Obs 60,891 75,911 60,891 75,911 $$R^{2}$$ 0.007 0.024 0.018 0.030 People 15,232 15,232 15,232 15,232 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ log(Wages + 1) log(Wages + 1) Coefficient (1) (2) (3) (4) $$\beta$$ 0.0051** 0.0059*** 0.0364*** 0.0398*** (0.002) (0.002) (0.013) (0.013) Post-period (years) 1 2 1 2 Obs 60,891 75,911 60,891 75,911 $$R^{2}$$ 0.007 0.024 0.018 0.030 People 15,232 15,232 15,232 15,232 This table shows the output of a regression that estimates the effect of longer retention time of nonpayment flags on the probability of receiving any wage income during the year. The table shows contains the coefficient $$\beta$$ from \begin{align*} 1\left(Wages>0\right){}_{i,t}&=\, \omega_{i} + \omega_{t} + \omega_{\tau} \nonumber\\ &\quad + \beta Exposuremonths_{i}\times New_{i}\times Post_{i,t} \nonumber\\ &\quad + \delta Post_{i,t} + \gamma New_{i}\times Post_{i,t} \nonumber\\ &\quad + \sum_{\tau=1,3,5,7}\lambda_{\tau}1\left(Exposuremonths_{i}=\tau\right)\times Post_{i,\tau} \nonumber\\ &\quad + \varepsilon_{i,t}. \end{align*} There are 15,232 people in this sample instead of 12,664 like in previous tables because we include the June–July cohort of defaulters, a cohort not included in the previous tests to balance people with high and low exposure with the longer retention time. Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 6 Employment outcomes with varying treatment intensity $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ log(Wages + 1) log(Wages + 1) Coefficient (1) (2) (3) (4) $$\beta$$ 0.0051** 0.0059*** 0.0364*** 0.0398*** (0.002) (0.002) (0.013) (0.013) Post-period (years) 1 2 1 2 Obs 60,891 75,911 60,891 75,911 $$R^{2}$$ 0.007 0.024 0.018 0.030 People 15,232 15,232 15,232 15,232 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ log(Wages + 1) log(Wages + 1) Coefficient (1) (2) (3) (4) $$\beta$$ 0.0051** 0.0059*** 0.0364*** 0.0398*** (0.002) (0.002) (0.013) (0.013) Post-period (years) 1 2 1 2 Obs 60,891 75,911 60,891 75,911 $$R^{2}$$ 0.007 0.024 0.018 0.030 People 15,232 15,232 15,232 15,232 This table shows the output of a regression that estimates the effect of longer retention time of nonpayment flags on the probability of receiving any wage income during the year. The table shows contains the coefficient $$\beta$$ from \begin{align*} 1\left(Wages>0\right){}_{i,t}&=\, \omega_{i} + \omega_{t} + \omega_{\tau} \nonumber\\ &\quad + \beta Exposuremonths_{i}\times New_{i}\times Post_{i,t} \nonumber\\ &\quad + \delta Post_{i,t} + \gamma New_{i}\times Post_{i,t} \nonumber\\ &\quad + \sum_{\tau=1,3,5,7}\lambda_{\tau}1\left(Exposuremonths_{i}=\tau\right)\times Post_{i,\tau} \nonumber\\ &\quad + \varepsilon_{i,t}. \end{align*} There are 15,232 people in this sample instead of 12,664 like in previous tables because we include the June–July cohort of defaulters, a cohort not included in the previous tests to balance people with high and low exposure with the longer retention time. Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. The coefficient of interest is $$\beta$$, which measures the average change in the probability of receiving wage income for each month of exposure. As the table shows, 1 month of exposure corresponds to approximately a 0.5% increase in the probability of receiving any wage income and about a 0.4% higher log wage income. This evidence are consistent with the hypothesis that past arrears affect the probability of being employed. As an additional test, in the Internet Appendix we plot the coefficients of a regression where we assign individual dummies to each bimonth of default throughout the year, in effect measuring effects of differential retention time across the bimonth of arrear. Consistent with our identification assumption, the measured effect is stronger for people who experienced greater reductions in retention times because of the month in which their default occurred, although standard errors are relatively large. Further, the pattern is monotonic for 3, 5, and 7 months of exposure. 2.4 Other results: Mobility and education We explore two additional margins that may be affected by changes in credit market information. First, we measure whether increased retention time affects an individual’s geographic mobility within Sweden.38 Because landlords commonly check a prospective lessee’s credit history before signing a lease agreement, we hypothesize that people may be more able to relocate if negative information is held by the credit registry for a shorter period. Moreover, improved access to employment opportunities may also induce mobility. We test this hypothesis in Columns 1 and 2 in Table 7 and define the outcome variable $$Relocates_{i,t}$$ as an indicator for whether an individual moved to a different municipality between years $$t-1$$ and $$t$$. In Column 1, we consider the treatment effect for the entire analysis sample and find that people who experienced a shorter retention time are 1.1 percentage points more likely to move, relative to a baseline mean of 7.7%. Although the coefficient is large in relative terms, it is not statistically significant at standard levels (p-value = .19). Given that people in our sample have very low home ownership rates (9.6%) and that credit checks for residential rental leases are common in Sweden, in column 2, we restrict the sample to the set of people who did not own a home in the preperiod. Here, we find that people who are not home owners are 1.6 percentage points more likely to move across postal codes when their negative credit market information is available to the credit market for less time. While the results are only significant at the 10% level, we find them highly suggestive of a type of mobility lock-in the rental market caused by credit market information.39 Table 7 Additional results: Mobility and education Relocates Relocates Years of schooling Coefficient (1) (2) (3) $$\beta$$ 0.0118 0.0159* –0.0355** (0.009) (0.009) (0.014) Post-period (years) 2 2 2 Sample (at event time 2) Full Nonhomeowners Full Obs 50,229 45,356 60,313 $$R^{2}$$ 0.001 0.001 0.015 People 12,664 11,441 12,414 Relocates Relocates Years of schooling Coefficient (1) (2) (3) $$\beta$$ 0.0118 0.0159* –0.0355** (0.009) (0.009) (0.014) Post-period (years) 2 2 2 Sample (at event time 2) Full Nonhomeowners Full Obs 50,229 45,356 60,313 $$R^{2}$$ 0.001 0.001 0.015 People 12,664 11,441 12,414 This table demonstrates effects of credit market information on household mobility and education. The table contains the coefficients and standard errors for our linear triple difference in difference estimations, using relocates, which is a dummy that equals one if an individual’s residence is in a different county and not missing from the previous event time year, and “years of schooling,” which measures the number of years of education as per the individual’s last completed level of education as outcomes. The number of observations is lower for “relocates” as it is defined in differences from the previous event time year, so the sample period only includes event times 1 through 4 (drops event time 0). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 7 Additional results: Mobility and education Relocates Relocates Years of schooling Coefficient (1) (2) (3) $$\beta$$ 0.0118 0.0159* –0.0355** (0.009) (0.009) (0.014) Post-period (years) 2 2 2 Sample (at event time 2) Full Nonhomeowners Full Obs 50,229 45,356 60,313 $$R^{2}$$ 0.001 0.001 0.015 People 12,664 11,441 12,414 Relocates Relocates Years of schooling Coefficient (1) (2) (3) $$\beta$$ 0.0118 0.0159* –0.0355** (0.009) (0.009) (0.014) Post-period (years) 2 2 2 Sample (at event time 2) Full Nonhomeowners Full Obs 50,229 45,356 60,313 $$R^{2}$$ 0.001 0.001 0.015 People 12,664 11,441 12,414 This table demonstrates effects of credit market information on household mobility and education. The table contains the coefficients and standard errors for our linear triple difference in difference estimations, using relocates, which is a dummy that equals one if an individual’s residence is in a different county and not missing from the previous event time year, and “years of schooling,” which measures the number of years of education as per the individual’s last completed level of education as outcomes. The number of observations is lower for “relocates” as it is defined in differences from the previous event time year, so the sample period only includes event times 1 through 4 (drops event time 0). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Improvements in mobility to better labor markets induced by the removal of bad credit information may have a causal role explaining the employment results. To test for this possibility, we perform a bounding exercise and find that this lock-in effect can explain at most 27% of the baseline effect of information on employment in Table 4.40 Again, the direction of causality may also flow in the opposite direction: a change in employment status may facilitate relocation. Thus, it is likely that mobility is not the main driver of the effects of credit information on employment and wages. Second, we ask whether some people respond to decreased labor market opportunities by adjusting their demand for additional schooling. When wage jobs become more scarce, the opportunity cost of schooling decreases, which may in turn increase the demand for schooling.41 This may be especially true in Sweden, where educational loans do not require credit checks and where the costs of education are relatively low. In Column 3 in Table 7, we find evidence that education is indeed one margin of adjustment used by people. Decreased retention time decreases the number of years of education by 0.0355. While the effect is small in magnitude, it is significant at the 5% level. Taken together, our results provide a consistent characterization of the effects of credit market information on labor markets. We interpret these results as the inverse of our baseline effects: information on past defaults reduces the probability that an individual is and remains employed. People respond to this decrease in employment opportunities by turning to self-employment activities and seeking additional education. As a result, people earn lower wages and lower total incomes 2 years after the information is removed from the credit registry. 3. Mechanisms and Additional Evidence 3.1 Credit information or credit supply? We document an economically large employment cost of default among people on the fringes of the labor and credit markets. Two possible channels could drive this effect. First, in the Internet Appendix, we show that credit supply increases when negative information is deleted.42 Thus, it is possible a priori that such an increase in credit supply might facilitate investments in job search or investment in labor productivity, which may lead to more employment. For example, credit may allow an individual to pay for a car repair, which in turn may improve punctuality at work. Second, employers might use credit information directly to screen workers. While both effects may be at play, we present five pieces of evidence that suggest that employer screening plays a key role above and beyond the role of credit supply in rationalizing our findings. First, recall that the magnitudes of the labor market earnings effects in Section 2.2 are four times larger than the commensurate increase in credit supply. Thus, for the credit effects to explain the entire earnings result, the labor market returns to capital would need to be on the order of 400%, an implausibly high number. Second, recall from Table 5 that improved credit information (and subsequent access to credit) leads to a reduction, rather than an increase, in self-employment activities. This result implies that a subset of people with bad credit records are unconstrained enough to pay any costs required to be self-employed. It seems unlikely that the costs of entering the labor market would be of a larger magnitude. Third, we study how the removal of negative credit information affects the employment of the individual’s spouse. Intuitively, if households are restricted in their access to credit, then a relaxation of credit constraints would also allow an individual’s spouse to supply more labor or invest in becoming more productive at work. At the margin, this would result in more employment for both the individual and the spouse. Although we cannot observe the spouse’s employment directly, for each individual in our sample we observe measures of household disposable income and individual disposable income. At the household and individual levels, disposable income is calculated by our data provider by adding up all income sources and subtracting allowances for dependents (children) and adjusting for the cost of living in a particular area. From these measures, we construct the spouse’s disposable income by subtracting the individual’s disposable income from the household’s disposable income.43 In Columns 1, 2, and 3 in Table 8 we present the output of regression (1) using as outcomes the individual’s disposable income, the household total disposable income, and the spouse’s disposable income, respectively. The spouse’s disposable income can be negative due to government transfers and adjustments, which makes it impossible to use a logarithm plus one approach.44 We restrict the sample of people to those that appear as nonsingle as of event time 2, whose measures of household and individual disposable income are different. Although potentially underpowered, these tests show that the individual’s and household’s disposable incomes increase when their information on past defaults is removed.45 However, Column 3 shows that the spouse’s disposable income does not vary in a statistically significant manner with negative credit information, and, if anything, the point estimate is negative. This evidence suggests that access to credit, brought about through deletion of negative information, does not necessarily relax household-level credit constraints that prevent access to labor markets. This nonresult, which we interpret with caution given potential issues with statistical power, is perhaps even more surprising given that the credit information of spouses is likely correlated due to joint accounts.46 Table 8 Effects on individual’s and spouse’s disposable income Ind. disp. inc. Hh. disp. inc. Spouse disp. inc. log(Ind. disp. inc. +1) log(Hh disp. inc.+1) Coefficient (1) (2) (3) (4) (5) $$\beta$$ 37.27* 34.25 –5.64 0.1204* 0.1466* (20.462) (26.307) (22.802) (0.068) (0.085) Post-period (years) 2 2 2 2 2 Obs 23,154 23,154 23,154 23,154 23,154 $$R^{2}$$ 0.026 0.021 0.002 0.003 0.002 People 4,667 4,667 4,667 4,667 4,667 Ind. disp. inc. Hh. disp. inc. Spouse disp. inc. log(Ind. disp. inc. +1) log(Hh disp. inc.+1) Coefficient (1) (2) (3) (4) (5) $$\beta$$ 37.27* 34.25 –5.64 0.1204* 0.1466* (20.462) (26.307) (22.802) (0.068) (0.085) Post-period (years) 2 2 2 2 2 Obs 23,154 23,154 23,154 23,154 23,154 $$R^{2}$$ 0.026 0.021 0.002 0.003 0.002 People 4,667 4,667 4,667 4,667 4,667 The table shows the regression output of our main regression model (1) using the individual’s disposable income (Column 1), the household’s disposable income (Column 2), and the spouse’s disposable income, calculated as the difference between the household’s and individual’s disposable income (Column 3). Variables are winsorized at the 99th percentile. In Columns 4 and 5, we use the logarithm of the individual’s disposable income and the household’s disposable income respectively, with zeros replace by one. The sample correspond to all people who are not single as of event time 2. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 8 Effects on individual’s and spouse’s disposable income Ind. disp. inc. Hh. disp. inc. Spouse disp. inc. log(Ind. disp. inc. +1) log(Hh disp. inc.+1) Coefficient (1) (2) (3) (4) (5) $$\beta$$ 37.27* 34.25 –5.64 0.1204* 0.1466* (20.462) (26.307) (22.802) (0.068) (0.085) Post-period (years) 2 2 2 2 2 Obs 23,154 23,154 23,154 23,154 23,154 $$R^{2}$$ 0.026 0.021 0.002 0.003 0.002 People 4,667 4,667 4,667 4,667 4,667 Ind. disp. inc. Hh. disp. inc. Spouse disp. inc. log(Ind. disp. inc. +1) log(Hh disp. inc.+1) Coefficient (1) (2) (3) (4) (5) $$\beta$$ 37.27* 34.25 –5.64 0.1204* 0.1466* (20.462) (26.307) (22.802) (0.068) (0.085) Post-period (years) 2 2 2 2 2 Obs 23,154 23,154 23,154 23,154 23,154 $$R^{2}$$ 0.026 0.021 0.002 0.003 0.002 People 4,667 4,667 4,667 4,667 4,667 The table shows the regression output of our main regression model (1) using the individual’s disposable income (Column 1), the household’s disposable income (Column 2), and the spouse’s disposable income, calculated as the difference between the household’s and individual’s disposable income (Column 3). Variables are winsorized at the 99th percentile. In Columns 4 and 5, we use the logarithm of the individual’s disposable income and the household’s disposable income respectively, with zeros replace by one. The sample correspond to all people who are not single as of event time 2. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Fourth, if people changed their job search behavior in response to improved access to credit, then we would expect increases in applications for both credit and jobs in response to the shortened retention time. In the Internet Appendix, we show that credit inquiries do increase following the deletion of negative information. While people are likely to be unaware of the exact timing of their information deletion, credit card companies and other lenders actively pursue people they deem to be creditworthy by monitoring credit records. However, there is no evidence that inquiries by nonfinancial institutions, which include employers, also increase. This evidence is more consistent with credit information affecting the demand for labor rather than the supply of labor. Fifth, and lastly, we exploit the information structure of the credit registries to further unpack the two potential mechanisms. In most countries, members of the credit registry—for example, banks and other financial institutions that share information about their borrowers—have access to all the information that is collected in the credit registry, but nonmembers—for example, employers, telephone and insurance companies and private people—do not.47 This asymmetry in information exists to provide members with incentives to report. Pertinently for our setting, employers cannot observe any details about an individual’s arrears, except whether an active nonpayment flag is present. Whereas banks are able to discriminate between a prospective borrower with ten arrears and a prospective borrower with only one arrear, employers observe identical information for a prospective employee with ten versus one arrear. If having fewer arrears is predictive of better repayment and better job performance, then both lenders and employers should want to use this information when making lending and hiring decisions. However, employers are unable to do so. This implies that in the credit market, people with fewer arrears should have less to gain from arrear flag deletion, while all people with nonpayment flags should experience similar employment screening benefits, regardless of the underlying number of arrears. In Table 9 we measure the credit and employment effects of arrear flag deletion separately for people with an above-median number of arrears and people with a below-median number of arrears. We measure the number of arrears at the time of the last nonpayment, in 2000 or in 2001 depending on the defaulting cohort. In our sample, people with above-median arrears experience the deletion of many arrears in response to the policy change, while people with only one arrear experience the deletion of that singular arrear in response to the policy change. The median number of arrears in the sample is five.48 Columns 1 and 2 in Table 9 show that the effect of the removal of the past nonpayment flag on the probability of receiving any wages is similar for people with many and few arrears. In Column 3 we run the main regression model with full interactions with an indicator for many arrears ($$Many_{i}$$). As expected, the coefficient on the interaction of the main treatment effect with $$Many_{i}$$ is small and insignificant. In contrast, Columns 4 and 5 show that the effect of the removal of the nonpayment flag on credit is positive and significant only for people with many arrears, and Column 6 shows that this difference is large and statistically significant. These patterns are, again, consistent with employer screening effects. If the employment effects were instead due strictly to improved access to credit, then we would expect symmetric patterns in labor and credit outcomes. Table 9 Differential effects by number of arrears $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Consumer Consumer Consumer Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0302* 0.0285* –103.38 967.34*** (0.017) (0.015) (416.697) (338.059) Interaction –0.0016 1,070.73** (0.023) (536.56) Post-period (years) 2 2 2 2 2 2 Sample Few arrears Many arrears All Few arrears Many arrears All Obs 31,346 31,242 63,113 31,767 31,659 62,901 $$R^{2}$$ 0.023 0.017 0.025 0.026 0.020 0.019 People 6,291 6,373 12,664 6,291 6,373 12,664 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Consumer Consumer Consumer Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0302* 0.0285* –103.38 967.34*** (0.017) (0.015) (416.697) (338.059) Interaction –0.0016 1,070.73** (0.023) (536.56) Post-period (years) 2 2 2 2 2 2 Sample Few arrears Many arrears All Few arrears Many arrears All Obs 31,346 31,242 63,113 31,767 31,659 62,901 $$R^{2}$$ 0.023 0.017 0.025 0.026 0.020 0.019 People 6,291 6,373 12,664 6,291 6,373 12,664 This table shows differential effects of credit information on employment and credit by the number of arrears at default. The table shows the regression output of our main regression model (1) for different subsamples. Columns 1 and 4 restrict the sample to people who had the median (five) or less arrears at the time of the last default, and Columns 2 and 5 restrict the sample to those with more arrears than the median. Columns 3 and 6 use the entire sample and run the main regression model Equation (1) where all right-hand-side variables are interacted with a dummy that equals one for people with many arrears at the time of the last nonpayment. Outcomes include $$1(wages>0)$$, a dummy for positive wages, and consumer, which measures the level of consumer credit in Swedish Kronor. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 9 Differential effects by number of arrears $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Consumer Consumer Consumer Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0302* 0.0285* –103.38 967.34*** (0.017) (0.015) (416.697) (338.059) Interaction –0.0016 1,070.73** (0.023) (536.56) Post-period (years) 2 2 2 2 2 2 Sample Few arrears Many arrears All Few arrears Many arrears All Obs 31,346 31,242 63,113 31,767 31,659 62,901 $$R^{2}$$ 0.023 0.017 0.025 0.026 0.020 0.019 People 6,291 6,373 12,664 6,291 6,373 12,664 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ Consumer Consumer Consumer Coefficient (1) (2) (3) (4) (5) (6) $$\beta$$ 0.0302* 0.0285* –103.38 967.34*** (0.017) (0.015) (416.697) (338.059) Interaction –0.0016 1,070.73** (0.023) (536.56) Post-period (years) 2 2 2 2 2 2 Sample Few arrears Many arrears All Few arrears Many arrears All Obs 31,346 31,242 63,113 31,767 31,659 62,901 $$R^{2}$$ 0.023 0.017 0.025 0.026 0.020 0.019 People 6,291 6,373 12,664 6,291 6,373 12,664 This table shows differential effects of credit information on employment and credit by the number of arrears at default. The table shows the regression output of our main regression model (1) for different subsamples. Columns 1 and 4 restrict the sample to people who had the median (five) or less arrears at the time of the last default, and Columns 2 and 5 restrict the sample to those with more arrears than the median. Columns 3 and 6 use the entire sample and run the main regression model Equation (1) where all right-hand-side variables are interacted with a dummy that equals one for people with many arrears at the time of the last nonpayment. Outcomes include $$1(wages>0)$$, a dummy for positive wages, and consumer, which measures the level of consumer credit in Swedish Kronor. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. The findings illustrate that banks likely adjust their underwriting decisions according to the severity of an individual’s past defaults. In contrast labor markets are unable to do so and are forced to pool all people with a nonpayment flag. Unless the information contained in the number of arrears is relevant for banks but not for employers, then the labor cost of default imposed by credit information may be excessive for those people with few arrears, for example. Information asymmetry provided to credit and noncredit market participants may lead to inefficiency. Given that credit registries were largely designed to reduce information asymmetries in the credit market, their use in labor markets is likely only second best. 3.2 Incidence We end our analysis by asking, for which types of people are the employment effects of negative credit information strongest? This question is relevant both for policy makers and for academics learning about what the credit score may convey to employers. First, we study how the effects vary for people with different levels of education. In Table 10 we present results for two subsamples: people with 11 or fewer years of completed schooling (the median number of years of schooling), and people with more than 11 years of schooling. Columns 1 and 2 show that a shorter retention time strongly increases the probability of employment for people with little education, but it has almost no effect on people with many years of schooling (p-value of difference .035). Columns 3 and 4 show that this pattern is repeated for log wages (p-value of difference .095). Thus, the employment impact of negative credit information is felt more acutely by those with lower levels of education. Table 10 Heterogeneity by preperiod education levels $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$\log(Wages+1)$$ $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0440*** –0.0003 0.2982*** 0.0102 (0.013) (0.021) (0.091) (0.147) Post-period (years) 2 2 2 2 Sample (years) $$\leq11$$ $$>11$$ $$\leq11$$ $$>11$$ Obs 44,543 16,240 44,543 16,240 $$R^{2}$$ 0.022 0.042 0.029 0.051 People 8,914 3,249 8,914 3,249 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$\log(Wages+1)$$ $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0440*** –0.0003 0.2982*** 0.0102 (0.013) (0.021) (0.091) (0.147) Post-period (years) 2 2 2 2 Sample (years) $$\leq11$$ $$>11$$ $$\leq11$$ $$>11$$ Obs 44,543 16,240 44,543 16,240 $$R^{2}$$ 0.022 0.042 0.029 0.051 People 8,914 3,249 8,914 3,249 This table shows differential effects of credit information on employment depending on preperiod level of education. The table shows the regression output of our main regression model (1) for different subsamples: people with 11 or fewer completed years of schooling, and people with more than 11 years of schooling. Outcomes are positive wage income and $$\log(Wages+1)$$, where zeros have been replaced by 1, as defined previously. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 10 Heterogeneity by preperiod education levels $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$\log(Wages+1)$$ $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0440*** –0.0003 0.2982*** 0.0102 (0.013) (0.021) (0.091) (0.147) Post-period (years) 2 2 2 2 Sample (years) $$\leq11$$ $$>11$$ $$\leq11$$ $$>11$$ Obs 44,543 16,240 44,543 16,240 $$R^{2}$$ 0.022 0.042 0.029 0.051 People 8,914 3,249 8,914 3,249 $$1\left(Wages>0\right)$$ $$1\left(Wages>0\right)$$ $$\log(Wages+1)$$ $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0440*** –0.0003 0.2982*** 0.0102 (0.013) (0.021) (0.091) (0.147) Post-period (years) 2 2 2 2 Sample (years) $$\leq11$$ $$>11$$ $$\leq11$$ $$>11$$ Obs 44,543 16,240 44,543 16,240 $$R^{2}$$ 0.022 0.042 0.029 0.051 People 8,914 3,249 8,914 3,249 This table shows differential effects of credit information on employment depending on preperiod level of education. The table shows the regression output of our main regression model (1) for different subsamples: people with 11 or fewer completed years of schooling, and people with more than 11 years of schooling. Outcomes are positive wage income and $$\log(Wages+1)$$, where zeros have been replaced by 1, as defined previously. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. One possible interpretation of this heterogeneity is that past credit information is only one of many signals used by employers to infer an individual’s unobserved productivity. For well-educated people, this information may be less relevant than other types of information (such as experience), and as such it may be down-weighted by employers. People with little formal education may also have fewer ways to signal their types.49 Second, we explore whether the effects differ by employment history, namely the preperiod (event time 2) employment status.50 Both the previously unemployed and previously employed may experience negative impacts. For example, negative credit information may hinder the ability of unemployed people to find work. This might also be the case for the many underemployed and part-time workers coded as previously employed in our sample.51 However, people with long prior unemployment spells may already be severely handicapped in the labor market (e.g., Kroft, Lange, and Notowidigdo 2013), even in the absence of negative credit information, and may have stopped their active job search. Thus, the additional impact of negative credit market information may be muted for this group. In Columns 1 and 2 in Table 11, we run our main specification (1) separately for those employed and unemployed at event time 2 (i.e., the year before arrear removal), respectively. We find similar positive effects on wage employment and on log wages for both groups (these results are statistically indistinguishable). In Columns 3 and 4, we further subdivide the previously unemployed into chronically and nonchronically unemployed. We define the chronically unemployed to be those without employment at event time 2 and who additionally worked at most 1 year out of the the 3 pre-period years. We find that the effects on formal employment and $$\log(Wages + 1)$$ are relatively small in magnitude (indeed, indistinguishable from zero) for the chronically unemployed, while the effects are large in magnitude for the nonchronically unemployed (p-value of difference on $$\log(Wages + 1)$$ .114). While underpowered, the differences in magnitudes are nonetheless striking. These results suggest that credit information may be most informative when people do not have other ways to signal their productivity. Long unemployment spells may provide employers with information that makes credit records superfluous. Table 11 Heterogeneity by preperiod employment history Panel A: $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0336** 0.0319* 0.0196 0.0578* (0.014) (0.016) (0.019) (0.030) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.050 0.016 0.009 0.065 People 5,424 6,942 4,819 2,123 Panel B: $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.2704** 0.1970* 0.0761 0.4505** (0.109) (0.107) (0.124) (0.202) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.072 0.018 0.014 0.067 People 5,424 6,942 4,819 2,123 Panel A: $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0336** 0.0319* 0.0196 0.0578* (0.014) (0.016) (0.019) (0.030) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.050 0.016 0.009 0.065 People 5,424 6,942 4,819 2,123 Panel B: $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.2704** 0.1970* 0.0761 0.4505** (0.109) (0.107) (0.124) (0.202) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.072 0.018 0.014 0.067 People 5,424 6,942 4,819 2,123 This table shows differential effects of credit information on employment depending on preperiod employment status. The table shows the regression output of our main regression model (1) for different subsamples. In panels A and B, Column 1 restricts the sample to people who are employed ($$Employed_{i,t}=1$$) as of event time 2, the year before their information on nonpayments is removed. Column 2 restricts the sample to people who are unemployed as of event time 2. Columns 3 and 4 split the sample of unemployed people. Column 3 restricts the sample to people who are chronically unemployed as of event time 2, defined as those people who have been unemployed for 2 or more years in the 3-year preperiod. Column 4 restricts to unemployed people who are not chronically unemployed. Panel A uses a dummy for positive wage income as outcome. Panel B uses $$\log(Wages + 1)$$, where zeros have been replaced by 1, as outcome. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Table 11 Heterogeneity by preperiod employment history Panel A: $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0336** 0.0319* 0.0196 0.0578* (0.014) (0.016) (0.019) (0.030) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.050 0.016 0.009 0.065 People 5,424 6,942 4,819 2,123 Panel B: $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.2704** 0.1970* 0.0761 0.4505** (0.109) (0.107) (0.124) (0.202) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.072 0.018 0.014 0.067 People 5,424 6,942 4,819 2,123 Panel A: $$1\left(Wages>0\right)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.0336** 0.0319* 0.0196 0.0578* (0.014) (0.016) (0.019) (0.030) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.050 0.016 0.009 0.065 People 5,424 6,942 4,819 2,123 Panel B: $$\log(Wages+1)$$ Coefficient (1) (2) (3) (4) $$\beta$$ 0.2704** 0.1970* 0.0761 0.4505** (0.109) (0.107) (0.124) (0.202) Post-period (years) 2 2 2 2 Sample $$\quad$$ (at event time 2) Employed Unemployed Unemployed: Chronic Unemployed: Nonchronic Obs 27,114 34,682 24,071 10,611 $$R^{2}$$ 0.072 0.018 0.014 0.067 People 5,424 6,942 4,819 2,123 This table shows differential effects of credit information on employment depending on preperiod employment status. The table shows the regression output of our main regression model (1) for different subsamples. In panels A and B, Column 1 restricts the sample to people who are employed ($$Employed_{i,t}=1$$) as of event time 2, the year before their information on nonpayments is removed. Column 2 restricts the sample to people who are unemployed as of event time 2. Columns 3 and 4 split the sample of unemployed people. Column 3 restricts the sample to people who are chronically unemployed as of event time 2, defined as those people who have been unemployed for 2 or more years in the 3-year preperiod. Column 4 restricts to unemployed people who are not chronically unemployed. Panel A uses a dummy for positive wage income as outcome. Panel B uses $$\log(Wages + 1)$$, where zeros have been replaced by 1, as outcome. The post-period includes 2 years after information is deleted (event times 3 and 4). Standard errors in parentheses are clustered at the individual level. *, **, and *** represent significance at the 10%, 5%, and 1% level, respectively. Finally, in the Internet Appendix, we show that the employment effect of shorter retention times is concentrated in geographical areas with low unemployment. Although again the test may be underpowered, one interpretation of this result is that the employment cost of default is more severe for “bad” people in “good times” (i.e., low unemployment areas) than for average households in high unemployment areas. Further, it is possible that the signal of productivity provided by credit information becomes more valuable when labor markets are tighter. 52 4. Conclusion We combine a unique natural experiment in Sweden with detailed credit and labor market data to document that credit market information has economically important effects that spill over onto other domains of a borrower’s life, namely success in the labor market. We focus on a marginal population, one that is likely to experience financial distress and unemployment, for whom exclusion from the credit and labor markets is likely quite costly, and to whom policy makers tend to pay close attention. We find robust evidence that an earlier deletion of negative credit information makes people more likely to be employed, and as a result, they earn higher incomes. These results highlight an understudied interlinkage between credit and labor markets. These results complement and contrast with findings by Cohen-Cole, Herkenhoff, and Phillips (2016b) and Dobbie et al. (2016), suggesting the effects of bad credit records are likely to be heterogeneous and depend on the type of credit information being reported and on the population under study. We also show that when labor market opportunities become scarce, people seek out self-employment and schooling as alternatives. These results indicate that for our sample of low income Swedes, self-employment is often an inferior alternative to the wage labor market. This finding resonates with the narrative in the entrepreneurship literature that many businesses owned by low income groups are not primed for transformative growth. The schooling response to the unemployment caused by negative credit information is also consistent with prior literature. While credit supply is also responsive to the deletion of negative credit information, we further provide evidence that a large portion of our estimated effects is likely explained by employer screening, a practice that has increased dramatically over the past decade and that has garnered the attention of many policy makers. Our results present some of the first causal evidence that in vulnerable populations, negative credit information can indeed impede success in the labor market. This implies that a temporary shock that causes an individual to default may have lasting and profound consequences. These results also imply that damage from credit information errors may be amplified through the labor market channel.53 Further, it may be difficult for households to use labor supply to smooth consumption when their credit record is poor. We also find suggestive evidence that asymmetries in the information available to noncredit entities may cause inefficiencies in the use of credit information. Our paper estimates the employment costs of default for a particularly vulnerable population, which is an important input for for modeling unsecured credit markets (e.g., Chatterjee et al. 2007; Livshits, MacGee, and Tertilt 2007) and for the policy debate. On these vulnerable populations, credit information could induce multiplier effects on unemployment (e.g., duration dependence) and potentially lead to poverty traps (Banerjee and Duflo 2012; Kroft, Lange, and Notowidigdo 2013). However, we acknowledge that a full welfare analysis of employer credit screening policies requires many additional inputs and several questions remain unanswered. For example, what are the countervailing benefits from using credit information on the efficiency of matching between firms and employees? Does the employment cost of default strengthen repayment incentives and result in deeper financial markets?54 These are all important questions for future work. Some contemporaneous studies have begun to address these questions. For example, Balance, Clifford, and Shoag (2016) show that state-level bans on credit checks by employers increased employment but caused a deterioration of labor market outcomes of particularly vulnerable populations. Bartik and Nelson (2016) and Cortes, Glover, and Tasci (2016) exploit the same regulation changes to find evidence of an average deterioration of labor markets, particularly for minorities, coupled with an increased demand from employers for alternative signals of applicants’ productivity, such as education. These studies suggest that banning the use of credit information in hiring decisions may harm the labor market outcomes of vulnerable populations and potentially reduce welfare. While we do not attempt such a welfare analysis, our results can provide guidance to policy makers regarding other types of interventions that might or might not limit the negative labor market consequences from experiencing a negative shock. We find very little evidence to indicate that access to credit alone dramatically improves access to labor markets. This suggests that policies such as social transfers or subsidized government credit would be unlikely to lead to large employment benefits. Instead, policy makers might want to consider policies that either help people to improve their credit records, such as credit counseling, or that help people to improve the noncredit information that they can report to prospective employers. Our results suggest that negative credit information is most detrimental for those workers with fewer alternate signals that employers can use for screening.55 We thank the editor Andrew Karolyi; the anonymous referees; Manuel Adelino, Tony Cookson, Nathan Hendren, Andrew Hertzberg, Wei Jiang, Emi Nakamura, Matthew Notowidigdo, Daniel Paravisini, Thomas Philippon, Enrique Seira, Nicolas Serrano-Velarde, Jose Tessada, Daniel Wolfenzon, and Jonathan Zinman; and numerous seminar and conference participants for helpful comments. Jesper Böjeryd provided excellent research assistance. Funding from VINNOVA is gratefully acknowledged. All errors are our own. Marieke Bos is also a visiting scholar at the Federal Reserve Bank of Philadelphia. The views expressed here are those of the authors and do not necessarily represent those of the Federal Reserve Bank of Philadelphia, or the Federal Reserve System. Supplementary data can be found on The Review of Financial Studies web site. Footnotes 1 For example, see Musto (2004), Brown and Zehnder (2007), Djankov, McLiesh, and Shleifer (2007), De Janvry, McIntosh, and Sadoulet (2010), Bos and Nakamura (2014), González-Uribe and Osorio (2014), Liberman (2016), and Dobbie et al. (2016). 2 In the United States, 47% of firms check the credit information of prospective employees (see http://www.shrm.org/research/surveyfindings/articles/pages/creditbackgroundchecks.aspx). In Sweden, where we conducted our empirical analysis, the leading credit registry estimates that roughly 15% of all the inquiries it receives are made by nonfinancial institutions conducting background checks on potential employees. These nonfinancial institutions employ approximately 37% of the Swedish labor force. On its Web site, the Swedish Government Employment Agency lists jobs that currently require a clean credit record: financial, transportation, real estate, retail, and security (see http://www.arbetsformedlingen.se). 3 Arrears, in turn, are inputs into the credit score. However, nonfinancial actors typically receive only a strict subset of the information housed in the credit registry and are not able to observe the credit score. In the United States, employers are not allowed to observe the FICO score or any other aggregated score. In Sweden, employers cannot see the summary credit score or other key details about the nature of the past delinquencies, but importantly, they do observe the nonpayment flag. 4 Screening by landlords may also contribute to the causal effect of information on employment by affecting mobility. We perform a bounding exercise and show that increased mobility following the removal of credit information can explain at most a quarter of the magnitude of our results. 5 See, for example, Karlan and Zinman (2009), Mullainathan and Shafir (2013), and Kehoe, Midrigan, and Pastorino (2016). 6 See Chatterji and Seamans (2012), Hombert et al. (2014), Greenstone, Mas, and Nguyen (2014), Schmalz, Sraer, and Thesmar (2017), and Adelino, Schoar, and Severino (2015). 7 See Low (2005), Pijoan-Mas (2006), Jayachandran (2006), and Blundell, Pistaferri, and Saporta-Eksten (2016). 8 Our results on the extensive margin of employment are also inconsistent with those of Herkenhoff (2013) and Cohen-Cole, Herkenhoff, and Phillips (2016a), who study a matching model of the labor market, where access to credit leads to higher unemployment through an increase in the employee’s outside option. Their model also suggests that wages are higher conditional on employment, a test we do not pursue given that conditioning on employment most likely leads to a selection bias in our setting. 9 We also find that our main effects are stronger among people with fewer years of schooling, consistent with a model in which employers choose to weigh multiple signals of productivity differentially. 10 That banks and nonfinancial institutions, like employers, have access to different sets of information is a prevalent feature of credit registries around the world, an asymmetry that arises to provide banks with incentives to report (Pagano and Jappelli 1993). 11 Aside from the empirical evidence cited above, theoretical contributions to this literature include Pagano and Jappelli (1993), Padilla and Pagano (2000), and Elul and Gottardi (2015), among others. 12 See, for example, Dobbie and Song (2015) and Liberman (2016). 13 For the policy debate, see, for example, the epigraph and Senator Elizabeth Warren and Representative Steve Cohen’s op-ed at http://webcache.googleusercontent.com/search?q=cache:http://blog.credit.com/2015/09/sen-warren-rep-cohen-its-time-to-stop-employer-credit-checks-125468/&gws_rd=cr&dcr=0&ei=bYwqWsa7GrLN6QS-rpfIBg. 14 Swedish banks typically report borrower default at 90 days past due. Other entities such as phone companies exercise discretion when a consumer is reported as delinquent. People have the option of filing an appeal to the courts to correct potential errors. 15 In particular, the law states that credit records are available to other parties as long as the explicit intent is to enter into a contractual relationship. Furthermore, a copy of their credit record and the identity of the requesting party is sent automatically to the individual whose information is requested. 16 The Swedish government announced their decision to change Paragraph 8 of the law that regulates the handling of credit information (KreditUpplysningsLagen or credit inquiry law) on July 2003, and the law change took effect in October 2003. See http://rkrattsdb.gov.se/SFSdoc/03/030504.PDF 17 In our bimonthly data, an individual who received an arrear on December 1 but had that arrear removed on December 31, is first observed without an arrear in February, 3 years later. 18 For example, people who lose their jobs and remain unemployed may have a higher propensity to default on their debts (Foote, Gerardi, and Willen (2008) and Gerardi et al. 2013). Further, loan repayment and job performance may both be affected by traits such as responsibility and trustworthiness. 19 Evidence consistent with this fact is presented graphically in the Internet Appendix. We plot the average probability of receiving any wages 2 years after their last default by the bimonth of default, for people in our sample who defaulted in 2000 or in 2001. The probability of employment varies between a max of 85% for February–March defaulters to a low of 77% for October–November defaulters. 20 See Bos, Carter, and Skiba (2012) for an extensive discussion of the household characteristics of pawn borrowers in Sweden compared with the full Swedish population and for a comparison of pawn borrowers in Sweden and in the United States. 21 Some people in our sample obtained a new arrear after this 20-month period. Thus, they maintain a nonpayment flag in their records after the original arrear received in 2000 or in 2001 is removed, which reduces the power of our tests. 22 The credit registry updates its information on a daily basis. The research team, however, was only allowed access to bimonthly snapshots of the data. 23 To make the early and late groups comparable in size, we exclude the June–July cohort. However, below we include people in this cohort when we measure differential effects by differential intensity of the treatment by month of nonpayment. 24 All our outcomes are at the yearly level, and any baseline variation in these levels that is driven by macroeconomic shocks is absorbed by the year fixed effects, $$\omega_{\tau}$$. 25 See http://www.statistikdatabasen.scb.se/pxweb/sv/ssd/START__LE__LE0101__LE0101S/LE01012013S22/?rxid=91289227-eae0-41b9-8da5-d9e7bbcf5e66. 26 See http://www.statistikdatabasen.scb.se/pxweb/sv/ssd/START__AM__AM0208__AM0208B/YREG26/?rxid=f45f90b6-7345-4877-ba25-9b43e6c6e299. 27 See http://www.arbetsformedlingen.se. 28 In the Internet Appendix we present plots of the average evolution of each outcome without differencing, that is, Old-Early, Old-Late, New-Early, and New-Late. 29 In the Internet Appendix we present a robustness result in which we exclude the individual fixed effects. Results are slightly larger in magnitude but are essentially unchanged from our main test. 30 Because of the panel nature of the data, we cluster standard errors at the individual level to avoid serial autocorrelation. One potential concern is that standard errors are serially correlated across bimonths of default. In the Internet Appendix, we present estimates of regression (1) using standard errors clustered at the bimonth of default by 5-year preperiod age groups (52 clusters). The significance is essentially unchanged relative to the main specification. 31 In the Internet Appendix we present the results of specifications with alternative transformations of the dependent variable (1) using the hyperbolic sine transformation as an alternative to replacing zeros in the logarithm and (2) using the level of wages. 32 We also find that the impacts on credit are short-lived and only last 1 year, while the earnings impacts persist across (at least) 2 years. 33 This corresponds to a 48% effect size on consumer credit (mean 1,879 SEK). In the preperiod, 75% of people in our sample have no consumer credit, likely from their negative credit information. 34 We obtain this fraction as follows. First, the average wage of people who transitioned from zero wages to positive wage income in event time 2, the year before the past default flag is removed, is 71,200 SEK. Thus, a 3% extensive margin effect from Column 4 in Table 4 corresponds to a wage effect of 2,129 SEK. Thus, the extensive margin represents $$\frac{2,129}{3,987}=53.4\%$$ of the total wage effect of 3,987 SEK shown in the Internet Appendix. 35 For example, the typically high level of unionization in Sweden contributes to a limited scope for adjustment along the wage margin. For statistics on the trade union density in Sweden, see, for example, https://stats.oecd.org/Index.aspx?DataSetCode=UN_DEN. 36 See Banerjee et al. (2015) for an application of this idea in India. 37 In this section, the sample includes people who defaulted in the June–July bimonth, an addition that increases the number of people and observations relative to previous tests. 38 In unreported results, we study the effect of negative credit information on the propensity of people in our sample to relocate. Consistent with past arrears reducing labor market opportunities, we find that people are slightly less likely to leave the country following the early deletion of their past defaults, although the effect is small. 39 This pattern is similar to the housing lock-in documented by Struyven (2014), who studies Dutch homeowners with high loan-to-value ratios. 40 We estimate this fraction as follows. We repeat the mobility regression result conditioning on people who moved and changed employment status, which implies a coefficient of 0.8%. If we fully attribute this coefficient to the causal effect of increased mobility following the early removal of credit information, then mobility can explain up to $$\frac{0.8\%}{3\%}=27\%$$ of the baseline effect on employment (denominator taken from Column 4 in Table 4). 41 See Charles, Hurst, and Notowidigdo (2015) for evidence of this idea in the United States. 42 In particular, we run our main specification (regression (1)), where the outcomes are $$1\left(Consumer>0\right)$$, a dummy for any consumer credit, and $$Consumer$$, the level of consumer credit. In both, the coefficient of interest is positive and highly significant. 43 We winsorize each of these variables at the 99th percentile. 44 These specifications using levels are comparable to the one we present in Table IAV (see the Internet Appendix) using wage as the outcome. 45 For comparability with our previous results, we present estimates using the logarithm of individual and household disposable income plus one on Columns 4 and 5 in Table 8 and note strongly significant effects of the removal of past of defaults on these outcomes, consistent with the evidence in the previous section. 46 Thus, it is possible that a spouse actually increases labor supply when the individual is unable to find a job because of negative credit information (Blundell, Pistaferri, and Saporta-Eksten 2016). 47 In the Internet Appendix, we include a figure that illustrates what information is available to members and nonmembers in Sweden. 48 We recognize that the number of arrears is not randomly assigned and may be correlated with other types of heterogeneity. Nonetheless, we find the results highly suggestive. 49 Low levels of education may also be correlated with other measures of labor market opportunities, such as industry or type of job. It might also be possible that different types of employers are more or less likely to use credit information when making hiring decisions. 50 We would have liked to explore other characteristics of an individual’s employment history. However, Statistics Sweden was unwilling to match other job characteristics such as type of job or industry of the employer to our credit information data set. 51 Our data set does not allow us to differentiate part-time from full-time employment. 52 It may also be the case that idiosyncratic shocks are punished more severely than are aggregate shocks. 53 For example, see http://www.forbes.com/sites/halahtouryalai/2013/12/17/should-your-credit-score-matter-on-job-interviews-senator-warren-says-no-aims-to-ban-employer-credit-checks/. 54 For example, people may want to continue to service underwater mortgages if the labor market costs are sufficiently high. Extrapolating to a different market and context, labor market costs may help to explain why strategic default was not common during the housing crisis (Foote, Gerardi, and Willen 2008). 55 These findings are consistent with those of Pallais (2014), who measures benefits to future employment from certification by previous employers in an online labor market. References Adelino, M., Schoar, A. and Severino. F. 2015 . House prices, collateral, and self-employment. Journal of Financial Economics 117 : 288 – 306 . Google Scholar CrossRef Search ADS Balance, J., Clifford, R. and Shoag. D. 2016 . “No more credit score” employer credit check banks and signal substitution. Working Paper . Banerjee, A., Breza, E. Duflo, E. and Kinnan. C. 2015 . Do credit credit constraints limit entrepreneurship? heterogeneity in the returns to micronance. Working Paper . Banerjee, A., and Duflo. E. 2012 . Poor economics: A radical rethinking of the way to ght global poverty . 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Published: Jan 23, 2018

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