Peer effects in employment status: Evidence from housing lotteries

Journal of Urban Economics 113 (2019) 103195

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Peer effects in employment status: Evidence from housing lotteries Ayako Kondo a, Masahiro Shoji b,∗ a b

Institute of Social Science, University of Tokyo, 7-3-1 Hongo, Bunkyo-ku, Tokyo 113-0033, Japan Faculty of Economics, Seijo University, 6-1-20 Seijo, Setagaya-ku, Tokyo 157-8511, Japan

a r t i c l e JEL codes: J20 J64 Keywords: Peer effect Employment Natural experiment

i n f o

a b s t r a c t Does a high peer employment rate increase individual employment probability? We exploit the random assignment of temporary housing to evacuees of the Fukushima Daiichi nuclear power plant accident to identify the effect of neighbors’ employment rates on an individual’s probability of finding a job post-evacuation. Using unique survey data, we find that a one percentage-point increase in the initial employment rate of an individual’s peers increases the probability of employment after six months by about 0.2 percentage points. We also show suggestive evidence to indicate that the social norm to work serves as an underlying mechanism of the observed peer effect despite data limitations.

1. Introduction Does a high employment rate among neighbors increase an individual’s employment probability? Previous studies show that neighborhood quality is strongly correlated with an individual’s labor market outcomes (Borjas, 1995; Cutler and Glaeser, 1997; Weinberg et al., 2004). However, well-known problems, such as self-sorting into neighborhoods, common shocks, and the reflection problem (Manski, 1993, 2000), make it difficult to identify the causal effect of neighbors’ employment rate. A few recent studies attempt to solve these problems using an instrumental variable for neighbors’ employment status (Maurin and Moschion, 2009) or controls for various fixed effects to absorb the self-sorting of neighbors (Bayer et al., 2008). However, experimental evidence from randomly assigned neighbors is still scarce in the context of peer effects in employment, unlike peer effects in student outcomes or workplace productivity. In this study, we exploit the random assignment of temporary housing to evacuees of the Fukushima Daiichi nuclear power plant accident to identify the effect of neighbors’ employment rate on the probability of finding a job after evacuation. After the accident caused by the Great East Japan Earthquake and subsequent tsunami, people living within a 30-km radius of the plant were forced to evacuate to other municipalities. Several months later, many of these evacuees were moved from emergency shelters to publicly provided temporary housing units allocated through a government lottery. This situation provided a rare opportunity to examine the causal effect of the peer employment rate using randomly assigned neighbors. We use unique survey data collected from 14 temporary housing clusters in Iwaki city, the largest and most populated city in Fukushima

∗

prefecture, 2.5 years after the accident. Among the 587 sampled individuals aged 20–69 years, 479 were not employed as of the end of March 2011, the month when the power plant accident occurred. We estimate the effect of the employment status of peers neighbors on duration to resuming work among evacuees. We find a significantly positive effect that is robust to various controls for individual characteristics and housing cluster fixed effects. The effect is not only statistically significant, but also economically substantial: the impact of an increase of one percentage point in the initial employment rate of an individual’s neighbors roughly corresponds to a 0.2 percentage-point increase in the probability of employment after six months. This study is built on the growing literature on neighborhood effects for people who are exogenously assigned to a new neighborhood. There are two strands of existing studies: social experiments that relocate randomly selected residents in poor neighborhoods to neighborhoods with lower poverty rates (e.g., the Moving-to-Opportunity [MTO] Program) and studies that examine refugee immigrants whose residential location in the host county is exogenously assigned. A comparison of these two strands suggests that the significance of neighborhood effects may depend on the degree to which the randomly assigned residents can maintain their sense of community with their peers. On the one hand, studies of MTO-type social experiments consider all residents in the neighborhood as the peer group. However, social interactions between program participants and peers may be infrequent given their different socioeconomic backgrounds. Previous studies consistently point out that adult participants feel isolated from new neighbors (Barnhardt et al., 2015); such studies typically find no improvement in outcomes for adults (Kling et al., 2007; Barnhardt et al., 2015). On the other hand, the peer group in refugee studies includes only

Corresponding author. E-mail addresses: [email protected] (A. Kondo), [email protected] (M. Shoji).

https://doi.org/10.1016/j.jue.2019.103195 Received 2 April 2018; Received in revised form 24 September 2019 Available online 25 September 2019 0094-1190/© 2019 Elsevier Inc. All rights reserved.

A. Kondo and M. Shoji

immigrants in the neighborhood, who share similar backgrounds. The sense of community may be strong with such peers and social interactions may be frequent. Previous studies indeed demonstrate significant influences from peers. Damm (2014) finds that labor market outcomes for refugee immigrants to Denmark were affected by the average skill level of non-Western immigrants living in the neighborhood rather than the overall population of the neighborhood. Studies of ethnic enclaves of refugee immigrants (Edin et al., 2003; Damm, 2009) also suggest that neighbors who share the same ethnic background affect immigrants’ labor market performance. Our findings of significant effects among evacuees lend support to this role of the sense of community, since all the residents of a temporary housing cluster are from the same municipality and aware that the community in the cluster is enduring. However, this study has three distinctive features compared with previous studies on refugee immigrants. The first critical difference is that previous studies examine how local neighbors affect new migrants, whereas we focus on how new migrants affect each other. It is frequently observed that new communities are formed exclusively by new migrants (e.g., refugee camps, temporary housing for victims of natural disasters, and school dormitories). Nevertheless, empirical evidence of peer effects in employment among such new migrants is scarce compared with studies of the influence of local neighbors on new migrants. The second key difference is access to the formal job market. On the one hand, since refugee immigrants have a different cultural background and speak a different language from people in the host country, they may have poor access to formal job search. On the other hand, forced evacuees should have the same access as locals to the formal job market since they have been relocated within the same prefecture and speak the same language.1 The third feature is financial assistance provided to the evacuees. The evacuees benefited from extended unemployment insurance for 210 days and compensation from the electric company, which may have resulted in lowered financial incentives to work and allowed them to delay their job search. All these features could affect the underlying mechanisms behind the observed effect of neighbors’ employment rate on an individual’s employment probability. We consider three potential channels driving the observed peer effect2 : joint consumption, the social norm to work, and residence-based job information networks including both direct referrals and other information sharing. In the context of the effect of local neighbors on new migrants, the social norm to work may not be important, because the neighbors know that their unfamiliarity with the local labor market makes it difficult for new migrants to find jobs. Instead, existing studies have shown that residence-based job information networks play an important role in neighborhood effects from local residents to new migrants (Edin et al., 2003; Damm, 2009, 2014) and among local residents (Topa and Zenou, 2015). By contrast, all evacuees in our setting are on equal ground, that is, they were forced to move to Iwaki in March 2011. Thus, unemployed evacuees may feel pressure from peers who have already found jobs. Lack of financial incentive also increases the intrinsic motivation for normative behavior such as work (Benabou and Tirole, 2000; Bowles and Polania-Reyes, 2012; Festré, 2010; Rebitzer and Taylor, 2011). Thus, pressure from peers may be higher among those with less financial incentive to work. Conversely, the existence of substantial non-labor income may weaken the peer effect through the motive to join leisure activities with neighbors with decent jobs, especially if the amount of the assistance is large enough even for unemployed evacuees to afford to participate. 1 The participants of the MTO-type social experiments did not have language problems either. In this sense, the observed positive effects of neighbors’ employment rate in such a situation suggest the importance of the sense of community—even when formal channels for job search are available. 2 Hereafter, we use “peer effect” as a short-hand for the effect of neighbors’ employment rate on an individual’s employment probability regardless of the underlying mechanism and call the relevant group of neighbors a “peer group.”

Journal of Urban Economics 113 (2019) 103195

Consistent with these predictions, we show suggestive evidence against joint consumption and weakly supporting the social norm channel. Since our data lacks information regarding the jobs held at the time of survey, we cannot test whether residence-based job information networks also contributed to the observed peer effect. Nonetheless, there is no reason to rule out them, as they do not contradict with the social norm to work. The inconclusiveness about the underlying mechanism is a major limitation of this study. Despite this limitation, the resettlement of displaced people is an important policy issue. In particular disasters increase the unemployment rate (Groen and Polivka, 2008) and this is a critical concern of policymakers (US Bureau of Labor Statistics, 2006). However, few empirical studies suggest how employment can be restored. Our findings suggest that the employment rates of these individuals depend on the makeup of the groups in which they are resettled. The remainder of this paper is organized as follows: Section 2 introduces the detailed process of housing lotteries and explains how we define a peer group. Section 3 describes the data and summary statistics. The empirical strategy to estimate peer effects is presented in Section 4, and the results in Section 5. Section 6 further discusses the underlying mechanisms of the observed peer effect and shows suggestive evidence for the social norm to work. Section 7 provides our concluding remarks. 2. Background 2.1. Housing lotteries for forced evacuees in Fukushima The Fukushima Daiichi nuclear power plant accident – caused on March 11, 2011, by the Great East Japan Earthquake and a subsequent tsunami – forced over 100,000 citizens to evacuate. Citizens of the municipalities within a 30-km radius of the power plant were ordered to evacuate to outside areas; most of them headed to large cities in Fukushima, such as Iwaki, Aizu, and Koriyama. Our study site was Iwaki city, which is 30–60 km from the Fukushima Daiichi nuclear power plant. Iwaki is the largest city in Fukushima prefecture, with a population of about 340,000; it was one of the municipalities to accept a large number of forced evacuees. While the city provided 36 clusters of publicly provided temporary housing for 3500 households, housing for tsunami-affected Iwaki citizens amounted to only around 180 units. The rest were for forced evacuees from six radiationaffected municipalities: Futaba, Okuma, Tomioka, Naraha, Hirono, and Kawauchi. In Iwaki city the provision of temporary housing was slow and gradual owing to the vast amount of required housing and limited land availability. Although the occupancy of the first cluster was completed in May 2011, some clusters were still under construction even in the summer of 2012. While awaiting the construction of temporary housing, evacuees had to stay at emergency shelters such as schools and public halls. Given this delay in housing provision, some of the evacuees started work before moving into temporary housing. The allocation procedure for temporary housing for the forced evacuees had two important features that are relevant to the identification of peer effects in employment. First, because of right-to-use by municipalities for the housing clusters in Iwaki, residents in each housing cluster all came from the same municipality. Second, each municipality used a lottery to allocate housing to forced evacuees who had applied for temporary housing. The location of housing within the cluster was also randomly allocated through the lottery. Furthermore, relocation between lottery winners was prohibited and non-take-up was rare3 because those

3 We confirmed this with an evacuee who was the manager of a cluster for Hirono and currently worked for an NGO to support evacuees in Iwaki. One might think that many evacuees were simultaneously seeking other options, such as permanent relocation to other regions, while applying for temporary housing. However, in reality, those who moved

A. Kondo and M. Shoji

Journal of Urban Economics 113 (2019) 103195

Fig. 1. Timeline of temporary housing lottery.

who won the lottery for temporary housing units could not apply for other temporary housing. Fig. 1 illustrates the timeline of the lottery to allocate temporary housing. When the construction of a housing cluster was close to completion, each municipality announced the availability of housing units. Then, evacuees from the municipality that held the right-to-use applied for that housing. At this point, applicants knew the location of the housing cluster and the number of available units for each room type (e.g., one bedroom), but did not know the location of the assigned housing unit within the cluster. Also, evacuees knew the location and size of other temporary housing clusters that were planned for construction. Those selected through the lottery were allowed to move in after construction was completed and most of them did so within a few months.4 Those not selected had to wait for the next lottery opportunity. This provides us with a natural experiment to identify the peer effect in employment status. Since residents of clusters were randomly selected, employment status of neighbors at the time of move-in to their cluster is exogenously given. Furthermore, neighbors were originally from the same municipality and aware that it could take a long time or be difficult for them to return. We speculate that this helped ensure their sense of community and, therefore, promoted active social interactions among residents. By leveraging these circumstances, we can estimate the impact of the employment rate among peers at the time of move-in to the cluster on the probability that the initially unemployed evacuees restart work. One main concern is that some residents may have already moved out of the temporary housing before we conducted the household survey in September 2013, causing a systematic selection of the remaining residents. Although the share of households who have relocated from each temporary housing cluster before the survey is not available, the high occupancy rate suggests that few households moved out of temporary housing: The occupancy rate of temporary housing was as high as 94.8% as of September 2013 in Iwaki city. Furthermore, as we discuss in Appendix A1, the occupancy rate had been stable at over 90%

out of the region did so by summer 2011, before the completion of most of the temporary housing (press release by Fukushima prefecture http://www.pref.fukushima.lg.jp/uploaded/attachment/299981.pdf). Also, given the severe shortage of private housing and rapidly rising rents in Iwaki, few people preferred private housing in the same area to publicly provided temporary housing available for free. 4 As we explain in Appendix A1, except for the Minamidai housing cluster for Futaba citizens, all housing clusters filled up quickly after they became available. This implies that most of the residents of each housing cluster took the lottery at the same time, before construction was completed.

since the evacuees moved in for most of the clusters. Even in Hirono and Kawauchi, where the government’s evacuation order was lifted in January and March 2012, respectively, the mayors encouraged citizens to remain in the housing even after the evacuation order was lifted due to lingering uncertainty about the health impact of radiation. Consequently, the occupancy rates of the clusters for Hirono and Kawauchi were 91.9% and 94.3%, respectively (calculated based on press releases by Fukushima prefecture). These arguments suggest that the issue of relocation may not be crucial in our setting. These arguments suggest that selection bias may not be crucial in our setting. Furthermore, Appendix A3 presents various robustness tests including replication of main results using only the subsample of municipalities with evidence that few of their evacuees had already left their temporary housing. 2.2. Definition and measurement of peer employment We define each individual’s “peer group” as his or her neighbors living in the same block (sub cluster) excluding his or her own family members living in the same house. On average, each housing cluster is divided into 3.8 blocks, with around 34 households per block. As an example, Fig. 2 shows a map of the Rinjo cluster, one of the clusters in our sample, with 106 housing units divided into four blocks (A-D). To provide a specific image of the peer group, let us use a person living in housing unit A1-1. The peer group for this person is defined as those living in the 40 housing units in Block A, except his or her own family members living in A1-1. We define the peer group at the block level because individuals seem to associate mainly with block neighbors for several reasons. First, residents of the same block were required to often work together for the maintenance of public spaces and facilities in their cluster. Each cleaning task is assigned to a group of residents from a certain block; for example, Block A would be in charge of the main entrance of the cluster and Block B, the meeting room. Second, the randomized allocation of housing completely disassociated local communities that existed before the power plant accident. Thus, evacuees knew few people in the cluster when they moved in (Shoji and Akaike, 2018) so it is reasonable to presume that they initially communicated with only a few adjacent households. Third, some blocks were geographically isolated from others even within the same cluster. For example, Block A in Fig. 2 is separated from the other blocks by a ditch running through the cluster. Fourth, working-age adults did not have much opportunity to get to know evacuees in other blocks because they seldom participated in cluster-wide social events designed to encourage communication among the evacuees beyond blocks (Shoji and Akaike, 2014). Finally, there is also anecdotal evidence based on the authors’ field interviews that some

A. Kondo and M. Shoji

Journal of Urban Economics 113 (2019) 103195

Fig. 2. Example of a housing cluster map (Rinjo cluster).Note: Photo taken by the author.

evacuees were unaware for a long time that their friends had also moved into the same cluster because they were allocated to different blocks. Furthermore, by defining peer groups at the block level, we can control for cluster fixed effects, that otherwise could cause a spurious correlation between the peer employment rate and the individual’s own probability of taking a job after moving into the housing. For example, the residents of a cluster near a train station might have better access to job opportunities and thus would be more likely to restart work. By examining the block-level employment rate, controlling for cluster fixed effects, we can identify the causal effect of the neighbors’ employment rate on the probability of restarting work, when cluster characteristics are constant. One might still be concerned about the use of neighbors at the block level. In particular, individuals living near the border of a block may frequently communicate with neighbors in the other blocks. Therefore, the peer effect of one’s own block members may be smaller, and the effect of other block members may be larger for them than for those living within the block. It is not feasible to test whether the employment rates of residents in other blocks in the same cluster have a weaker effect than those of residents in the same block because, in our specification controlling for the cluster fixed effects, the employment rates of one’s own and other blocks are negatively correlated by construction.5 However, this mechanical negative correlation in employment rates between blocks ensures that the potential bias caused by the peer effects of other block members, if any, should attenuate the estimated peer effect.6

In theory, a peer group could also be defined as a group of individuals with similar demographic characteristics. However, the employment rate of peers defined in this way is not independent of an individual’s own characteristics because demographic characteristics are correlated with both the individual’s and peers’ employment rates. Furthermore, the sample size is too small to limit the range of peers to neighbors who have the same demographic characteristics. For example, the average number of neighbors with vocational or university degree is only 3. Given these arguments, we define the initial employment rate of peers of individual i’ in cluster c, peerci , as the ratio of peers who had restarted work by the month they moved into the temporary housing among all peers living on the same block at the time of the survey. Specifically, for each respondent aged 20–69 years, we generate a dummy indicator that takes the value of 1 if he or she had already restarted work before moving into temporary housing (i.e., the movein month is later than the month restarting work). Then, we take the average of this dummy indicator for all respondents in the same block except members of the respondent’s own household.7 Note that we use the employment status of each peer as measured at the time the peer (and not individual i) moved into the cluster. We do this because it is independent of the individual’s own characteristics. Admittedly what really matters is the employment rate of neighbors who were around at the time the individual moved in. However, the timing when individual i moved in is endogenous, and people who moved

𝑜𝑤𝑛

5

It is difficult to add the “adjacent blocks’ employment rate” as an explanatory variable because the definition of “adjacent blocks” is not straightforward. For example, in the cluster shown in Fig. 2, block A does not have an adjacent block if the space between block A and the other blocks is large. If the space is sufficiently small to ignore, then block C is adjacent to all other blocks in the cluster. Either way, it is difficult to assign an “adjacent blocks’ employment rate” for all blocks. 6 For simplification, let us consider a linear model: Y𝑐𝑖 = 𝛾 𝑜𝑤𝑛 𝑝𝑒𝑒𝑟𝑜𝑤𝑛 𝑐𝑖 + 𝛾 𝑎𝑑𝑗 𝑝𝑒𝑒𝑟𝑎𝑑𝑗 𝑐𝑖 + 𝜃𝑐 + 𝜀𝑐𝑖 where Yci represents the likelihood of restarting work for individual i living in cluster c, and 𝑝𝑒𝑒𝑟𝑜𝑤𝑛 and 𝑝𝑒𝑒𝑟𝑎𝑑𝑗 are the employment 𝑐𝑖 𝑐𝑖 rate of neighbors in the same block and the adjacent block(s). The positive spillover effect of the peer employment rate from adjacent blocks means 𝛾 adj > 0. By subtracting the cluster mean of each variable, this formula can be 𝑜𝑤𝑛 rewritten as the following within regression. Y𝑐𝑖 − Ȳ 𝑐 = 𝛾 𝑜𝑤𝑛 (𝑝𝑒𝑒𝑟𝑜𝑤𝑛 𝑐𝑖 − 𝑝𝑒𝑒𝑟𝑐 ) + 𝑎𝑑𝑗 𝑎𝑑𝑗 𝑎𝑑𝑗 𝛾 (𝑝𝑒𝑒𝑟𝑐𝑖 − 𝑝𝑒𝑒𝑟𝑐 ) + 𝜀𝑐𝑖 − 𝜀̄ 𝑐 Suppose that one of individual i’s peers in the

same block becomes employed. Then, 𝑝𝑒𝑒𝑟𝑜𝑤𝑛 increases. Although 𝑝𝑒𝑒𝑟𝑐 also 𝑐𝑖 𝑜𝑤𝑛 𝑜𝑤𝑛 increases, its change is smaller than the change of 𝑝𝑒𝑒𝑟𝑜𝑤𝑛 𝑐𝑖 , thus 𝑝𝑒𝑒𝑟𝑐𝑖 − 𝑝𝑒𝑒𝑟𝑐 𝑎𝑑𝑗 𝑎𝑑𝑗 increases. On the other hand, 𝑝𝑒𝑒𝑟𝑐𝑖 does not change, and 𝑝𝑒𝑒𝑟𝑐 increases because this newly employed individual is in someone else’s adjacent block. Thus, 𝑎𝑑𝑗 𝑝𝑒𝑒𝑟𝑎𝑑𝑗 decreases when a peer in the same block as individual i be𝑐𝑖 − 𝑝𝑒𝑒𝑟𝑐 𝑜𝑤𝑛 𝑎𝑑𝑗 comes employed. Hence, 𝑝𝑒𝑒𝑟𝑜𝑤𝑛 and 𝑝𝑒𝑒𝑟𝑎𝑑𝑗 are negatively 𝑐𝑖 − 𝑝𝑒𝑒𝑟𝑐 𝑐𝑖 − 𝑝𝑒𝑒𝑟𝑐 𝑎𝑑𝑗 correlated. Then, if 𝛾 adj > 0, omitting 𝑝𝑒𝑒𝑟𝑎𝑑𝑗 − 𝑝𝑒𝑒𝑟 will generate a negative 𝑐𝑖 𝑐 𝑜𝑤𝑛 own correlation between the error term and (𝑝𝑒𝑒𝑟𝑜𝑤𝑛 will be bi𝑐𝑖 − 𝑝𝑒𝑒𝑟𝑐 ). Thus, 𝛾 ased downward. Furthermore, in Appendix A2, we show that the magnitude of the peer effects from one’s own block members does not vary with the location of the housing unit in the block, suggesting that such bias seems to be small. 7 An anonymous reviewer pointed out the possibility of measurement errors due to recall bias in peerci . Although each individual’s response could include some measurement errors, such errors are unlikely to be correlated with other block members’ responses. Thus, if there is any bias in the coefficient of the peer employment rate, it should be an attenuation bias toward zero.

A. Kondo and M. Shoji

Journal of Urban Economics 113 (2019) 103195

Fig. 3. Active job openings to applicants ratio, December 2010–September 2013. Sources: Iwaki area: Monthly press releases by Fukushima Labor Bureau available at http://fukushima-roudoukyoku.jsite.mhlw.go. jp/jirei_toukei/koyou_toukei/koyou_situgyou.html (accessed 8/28/2015). Sum of three job placement offices in Iwaki city.National average: Monthly reports of the Employment Service Agency (shokugyo antei gyomu tokei), Ministry of Health, Labor and Welfare.

in later would face a higher peer employment rate simply because more people restart work over time. Therefore, we use the exogenous measure of peers’ initial employment status.8 In any case, as shown later, about three quarters of our sample moved into temporary housing within two months after completion of construction. Therefore, in practice, the difference between these two measures of peer employment is very small. As discussed in detail in Appendix A3, we limit our sample to those who moved in within two months after the completion of construction, as a robustness check, and find that the results do not change qualitatively. 2.3. Labor market conditions and financial disincentives to work Official statistics show that it was relatively easy for evacuees to find jobs in the city of Iwaki. Although the devastating earthquake and tsunami destroyed many jobs, reconstruction generated a large labor demand. Fig. 3 compares the active job openings to applicants ratio reported by public job placement agencies in the Iwaki area with the national average. The difference between the national average and Iwaki before the earthquake and power plant accident was negligible. After the quake, the ratio for Iwaki started to rise faster than the national average. It peaked at the end of 2012, and stayed significantly higher than the national average in subsequent years. While the number of job openings increased in most industries, the construction industry experienced by far the largest increase in labor demand. The number of new job openings in construction rose 2.5-fold from 2010 to 20119 and remained unchanged in 2012. In particular, a large number of workers 8

For example, suppose four people moved into the same block. Individual A moved in first, then B, then C, and D came last. A and D were working when they moved in, and B started to work after C moved in. In this example, the actual employment of neighbors that each individual faced when he or she moved in is undefined for A (because no neighbor existed), 100% for B (A was working), 50% for C (A was working, B was not), and 66% for D (A and B were working, C was not). However, we define peerci as 33% for A (D was working, B and C were not), 66% for B (A and D were working, C was not), 66% for C (A and D were working, B was not), and 33% for D (A was working, B and C were not). In this way, we can deal with the endogeneity that those who moved in later tend to face a higher employment rate of peers (in this example, B became employed before D moved in). 9 Number of job openings posted to Hello Work Taira, the largest public job placement agency in Iwaki city. Retrieved from the Fukushima Labour Bureau (2011).

were needed to clean up the radiation-affected areas, which did not require high-level skills. Among other industries, the number of new job openings rose 1.8-fold in manufacturing and 1.6-fold in the medical and welfare industries. Furthermore, the government subsidized firms that employed those from disaster-affected areas. Despite the relatively high labor demand, there were two financial disincentives for evacuees to work. First, the maximum duration of the unemployment benefit was extended by 210 days in the areas affected by the earthquake including Iwaki. Thus, evacuees who lost their jobs were able to receive unemployment benefits until the end of 2011. Second, financial compensation from the Tokyo Electric Power Company (TEPCO) may have had a negative income effect on labor supply. While there are many categories of compensation, the two most relevant were the compensation for mental distress and foregone income, both introduced in August 2011. The monthly compensation for mental distress was JPY 100,000 (about USD 130010 ) per person and it was to be paid until the evacuation order was lifted. The compensation for foregone income was determined by the income from the job lost due to the power plant accident. 3. Data 3.1. Survey design and sample selection In September 2013, we conducted a unique household survey of residents of the temporary housing clusters in Iwaki city. Survey households were selected using a stratified random sampling method. In the first step, we non-randomly selected 14 of 36 clusters based on cluster size and location and municipalities holding a right-to-use.11 We excluded clusters of evacuees from tsunami-affected areas in Iwaki from our sample because their assignment to temporary housing was not based on the lottery. In the second step, approximately 50% of the housing was

10

The exchange rate in 2011 was USD 1 = JPY 77. The criteria for cluster selection were as follows: (1) The sample covers all six municipalities evacuated to the city of Iwaki; (2) for municipalities constructing many clusters, multiple clusters were selected; (3) with multiple clusters for the same municipality, both large-scale (with a capacity of more than 100 households) and small-scale clusters were selected; and (4) for Naraha and Hirono municipalities, which constructed many clusters, clusters were selected from geographically scattered areas. 11

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Journal of Urban Economics 113 (2019) 103195

Table 1 Breakdown of survey households. Municipality

Sample size

Fraction in the sample (percentage)

Fraction in the total number of evacuees in Iwaki city (percentage)

Futaba Okuma Tomioka Naraha Kawauchi Hirono Iwakia Others Missing

30 70 100 185 15 115 – 2 1

5.8 13.5 19.3 35.8 2.9 22.2 – 0.4 0.2

7.4 18.7 12.9 33.8 1.5 21.3 4.4

Total

518

a

We exclude evacuees from tsunami-affected areas in Iwaki from our sample because their assignment to temporary housing was not based on the lottery. Table 2 Surveyed housing clusters and number of blocks in each cluster. Name of housing cluster

Completion

Municipality of origin

Number of blocks

Minamidai Shimoyada Kamikajiro Izumitamatsuyu Kamiyoshima Rinjo Uchigoshiramizu Takaku10 Takaku5 Takaku 9 Onigoe∗

8/2011 11/2011 5/2012 9/2011 6/2011 7/2012 10/2011 7/2011 6/2011 7/2011 10/2011

Takaku 2 Takaku 3 Takaku 4

6/2011 6/2011 6/2011

Futaba Okuma Okuma Tomioka Tomioka Naraha Naraha Naraha Naraha Naraha Kawauchi Hirono (Iwaki) Hirono Hirono Hirono

8 4 3 4 1 4 1 9 1 10 1 3 (1) 1 1 1

Note: The Kawauchi, Hirono, and Iwaki municipalities share the Onigoe cluster. Since the lottery was conducted within each municipality, in the analysis we treated blocks occupied by different municipalities as different clusters. The block occupied by Iwaki citizens is excluded from our analysis sample.

randomly selected in each cluster (784 of 1733 housing units). In the third step, vacant housing units were replaced with the next-door housing unless it was already selected in our sample. To minimize the nonresponse rate, particularly because of respondents working outside, we visited them multiple times, including in the evenings and on weekends. Ultimately, we visited 701 households and completed a survey with 518 of them.12 Table 1 presents a breakdown of the municipalities of sample households (column [3]) among total evacuee households in Iwaki (column [4]); as we can see, our sample is not biased toward a particular municipality. Table 2 lists the surveyed housing clusters and the number of blocks in each cluster. One cluster, Onigoe, was actually shared by three municipalities and since the housing lottery was conducted separately by each municipality for their share of cluster, we treat the blocks occupied by each municipality in Onigoe cluster as separate clusters. Although we interviewed one person per household, we collected basic information such as gender, age by 10-year category, and employment status, for all individuals living in the same household. The number of all individuals included in the data was 1117. Among them,

12 The non-response rate is 1-581/701=0.26. The correlation between the nonresponse rate at the block level and ratio of individuals who had already started work at the time of move-in was weak and statistically insignificant (correlation coefficient=−0.03, p-value = 0.85). Therefore, it is unlikely that we undersampled those with a job at the time of the survey.

we limited our sample to 587 individuals aged 20–69 years.13 Table 3 compares the demographic composition of these 587 individuals in our data with the population of the six municipalities where the evacuees lived before the power plant accident, based on the 2010 Population Census. Our sample is older than the baseline population, mainly because households with young children were more likely to move out of the region permanently or choose other options, such as leased housing financed by the government. Furthermore, the individuals in our sample were less likely to have university degrees because older cohorts are on average less educated. Among the 587 evacuees aged 20–69 years, 108 were working as of the end of March 2011, the month when the accident occurred. We assume they continued working at the same job14 and exclude them from the analyses sample15 although they are included in the computation of the peer employment rate at the time of move-in.

13 In Japan, “working-age” is usually defined as 15–65 years, but our survey asked for respondents’ ages in 10-year categories, and we limit our “workingage” sample to those aged 20–69. 14 We make this assumption because it was practically difficult to find a new job within 20 days of the earthquake, when people had to relocate to Iwaki during the confusion caused by the disaster. Since the six municipalities are within a one-hour drive of Iwaki city, many people commuted to Iwaki city before the power plant accident, and some of them were able to continue working. 15 Since our main empirical model is a hazard model, we cannot include those who were employed in the first period (i.e., not at risk).

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Table 3 Comparison between our sample and the Population Census before the accident. Our sample: all individuals aged 20–69 years as of September 2013 (N = 587) (shown in percentages)

Population Census: all individuals aged 20–69 years living in the six municipalities prior to the Great Japan Earthquake (shown in percentages)

years years years years years

10 13 16 22 39

16 20 19 25 21

Education Junior high school High school Vocational/Jr college University

19 60 14 6

14 61 12 12

Age 20–29 30–39 40–49 50–59 60–69

Note: The Population Census was conducted by the Statistic Bureau of Japan in October 2010. The numbers shown in the table are the averages for the six municipalities where the respondents of our original survey resided before the Great Japan Earthquake. Fig. 4. Kaplan–Meier survival estimates of restarting work.

3.2. Variables and summary statistics Our main outcome variable is the hazard associated with restarting work after the power plant accident. This variable was constructed from the month when the individual started working again. Fig. 4 summarizes the Kaplan–Meier survival function for the sample of those who had not yet restarted work as of the end of March 2011 (N = 479). As shown in the graph, men tended to restart work sooner than women did. About 51.6% of men and 24.3% of women had restarted work by the time the survey was conducted in September 2013. We take into account this gender difference in the hazard function. An important limitation of our data is the lack of a detailed employment history. We only ask the month he or she started working again after the power plant accident but we did not ask for detailed monthly employment states. Thus, we cannot identify those who resumed work but then subsequently quit. Furthermore, by design the survey did not ask for much detail on the current economic situation, such as earnings, occupation, and other job information as of the survey date, because of concern that such questions could offend evacuees who were forced to leave their homes and jobs. We also do not know to what extent an evacuee’s current job was related to the job held before the accident. This lack of detailed information on the job(s) held after the power plant

accident makes it difficult to pin down some of the underlying mechanisms. Table 4 shows the summary statistics by employment status as of the end of March 2011. The first column includes all individuals aged 20–69 years; this is the sample used to calculate the peer employment rate. The second column includes those who had not yet restarted work as of the end of March 2011, which is the sample used in the main analysis. For comparison, the third column includes those who continued to work. Panel A of Table 4 shows that those who continued working are more likely to be men, aged 40–59 years, more educated, in larger households, and engaged in construction and utility industries.16 On the other hand, damage to the house and loss of family members are uncorrelated with employment right after the accident. Nonetheless, we control for these variables because the level of damage from the earthquake and tsunami may affect labor supply by way of the amount of financial support provided by the government. Additionally, it may have some psychological

16 We combined utility with the construction industry because most workers in the utility industry in our sample were blue-collar workers doing maintenance and construction work. Both industries faced similar labor shortages for reconstruction work after the earthquake.

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Table 4 Summary statistics. All individuals aged 20–69 years (N = 587) Mean (1)

S.D. (2)

Employment status at the end of March 2011 Not working (N = 479)

Working (N = 108)

Mean (3)

Mean (5)

S.D. (4)

S.D. (6)

Panel A: Individual characteristics 1 if male Age (years) as of September 2013 20–29 (reference) 30–39 40–49 50–59 60–69 Education Junior high school (reference) High school Vocational/Junior college University Household size Housing loss None (reference) Partial Half Full 1 if lost household member(s) by the tsunami Work industry before the accident Not working Agriculture and fishery Construction/utility Manufacturing Sales and service Medical and nursing Others Change in expenditure for food since move-in Decreased (1–4) Unchanged (5) Increased (6–9) Change in expenditure for leisure since move-in Decreased (1–4) Unchanged (5) Increased (6–9) Respondents’ subjective well-being relative to other evacuees in the same clustera Unhappier than other evacuees (1–3) Neutral (4) Happier than other evacuees (5–7) Respondents’ subjective well-being relative to evacuees in other clustersa Unhappier than those in the other clusters (1–3) Neutral (4) Happier than those in the other clusters (5–7)

0.51

0.44

0.83

0.10 0.13 0.16 0.22 0.39

0.10 0.12 0.14 0.20 0.43

0.08 0.16 0.25 0.31 0.19

0.19 0.60 0.14 0.06 2.84

0.20 0.62 0.14 0.05 2.76

0.13 0.55 0.18 0.15 3.20

∗∗∗ ∗∗∗

∗∗∗

1.27

0.61

0.34 0.40 0.19 0.08 0.06

0.34 0.40 0.19 0.07 0.06

0.32 0.40 0.17 0.11 0.06

0.23 0.05 0.23 0.11 0.09 0.07 0.22

0.29 0.05 0.18 0.11 0.10 0.07 0.20

0.01 0.02 0.44 0.11 0.05 0.08 0.29

0.13 0.50 0.37

0.14 0.50 0.36

0.07 0.50 0.43

0.17 0.57 0.26

0.16 0.57 0.27

0.18 0.59 0.23

0.15 0.39 0.46

0.15 0.39 0.45

0.11 0.39 0.50

0.13 0.42 0.45

0.13 0.42 0.45

0.14 0.46 0.39

0.98

∗∗

∗∗∗

Panel B: Evacuation process Period of move-in to temporary housing (months since accident) Gap between construction completion and move-in 0–2 months 3–5 months 6–9 month 10–14 months 15–29 months

9.45

5.69

9.41

5.60

9.67

6.09

0.74 0.10 0.06 0.08 0.02

0.75 0.09 0.05 0.09 0.02

0.69 0.12 0.08 0.06 0.04

0.33

0.17

1.00

∗∗∗

0.51 0.14 0.48 15.6 0.32

0.30 0.08 0.36 15.7 0.31

1.00 1.00 1.00 15.5 0.33

∗∗∗

Panel C: Own and peers’ employment status Had restarted work by the time of move-in to temporary housing Males Females Restarted work by September 2013 Size of peer group in the same block Percentage of peers who had already started to work before they moved in (peeri )

8.4 0.16

8.4 0.15

∗∗∗

8.6 0.20

The asterisks in the last column indicate statistical significance of the difference between the sample who were working and not working: ∗ , ∗∗ , and ∗ ∗ ∗ indicate the significance level at 10%, 5%, and 1%, respectively. a Available only for the survey respondents. Sample size of age from 20 to 69: 291, not working: 263, working: 28.

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Journal of Urban Economics 113 (2019) 103195

Fig. 5. Kernel density of peers’ employment rate at the time of move-in.

effect. The measures of respondents’ consumption and subjective wellbeing are used in the analyses of underlying mechanisms in Section 6. Panel B summarizes the evacuation process. On average, evacuees moved into temporary housing 9.5 months after the accident, with no difference between those who continued working and those who did not. Furthermore, 74% of our sample moved into temporary housing within two months after completion of construction; thus, the average employment rate when each person in the peer group moved in should serve as a good proxy for the average employment status of the neighbors when the individual moved in. Panel C summarizes the individual’s own employment status and the peers’ employment rate. At the time of move in, about 33% of all evacuees aged 20–69 years had already restarted work. Among those who did not continue working right after the accident, 17% restarted work. As already shown in Fig. 4, men are more likely to restart work than women are. By the time of the survey in September 2013, 48% of all evacuees and 36% of those who did not work at the end of March 2011 had restarted work.17 As explained in Section 2.2, our key explanatory variable is peerci , the fraction of peers who had restarted work before they moved in. The variable is calculated using on all 587 individuals. The average number of peers in our data is 15.6,18 and the peers’ average employment rate is 32%. As expected from the random assignment of peers, these variables are uncorrelated with the individual’s own employment status. The standard deviation of peerci is 16%. Fig. 5 shows the kernel density.

17 These fractions are smaller than previous studies, such as that of Cingano and Rosolia (2012), who study workers displaced by firm closures in Italy, and Glitz (2017), who study workers displaced by establishment closures in Germany. This is partly because our sample included those who did not work before the accident. After excluding them, the fractions increased up to 59% and 47%, respectively. 18 Note that our data are based on a 50% random sample of housing cluster residents, not a complete survey, and 32% of the surveyed households did not include any individuals aged 20–69 years. Thus, although the average number of housing units per block was 34, the average number of peers in our data is 15.6. This variation in the number of housing units in each block could generate additional noise in the observed peer employment rate, but such noise should be uncorrelated with each individual’s likelihood of starting a job. This is because the lottery should allocate the block randomly, and the block size or its sampling rate is unlikely to affect employment probability. We thank an anonymous reviewer for pointing this out.

4. Empirical model to estimate peer effects To identify the causal effect of peerci – the employment rate of neighbors at the time of move-in, as defined above – on the hazard of restarting work, we estimate the following Cox proportional hazard model: ( ( ) ) 𝑏𝑒𝑓 𝑏𝑒𝑓 h t|𝑝𝑒𝑒𝑟𝑐𝑖 , sex𝑐𝑖 , 𝑋𝑐𝑖 = λ t; sex𝑐𝑖 exp(𝑋𝑐𝑖 𝛽 + 𝑝𝑒𝑒𝑟𝑐𝑖 𝐷𝑐𝑖𝑡 𝛾 1𝑦𝑟 1𝑦𝑟 0_5 0_5 6_11 6_11 + 𝑝𝑒𝑒𝑟𝑐𝑖 𝐷𝑐𝑖𝑡 𝛾 + 𝑝𝑒𝑒𝑟𝑐𝑖 𝐷𝑐𝑖𝑡 𝛾 + 𝑝𝑒𝑒𝑟𝑐𝑖 𝐷𝑐𝑖𝑡 𝛾 + 𝜃𝑐 )

(1)

The hazard of restarting work, h(t|peerci , sexci , Xci ), is the probability density associated with individual i in cluster c restarting work in the tth month after March 2011, when the power plant accident occurred, conditional on not having resumed working since March 2011.19 Our sample includes the 85 individuals who started working again after the accident but before moving into temporary housing. This is to avoid potential biases arising from left censoring of the sample.20 We allow the effect of peerci to vary with the number of months since the individual moved into the temporary housing cluster. Specifically, 𝑏𝑒𝑓 1𝑦𝑟 0 _5 6_11 we interact peerci with four dummy variables, 𝐷𝑐𝑖𝑡 , 𝐷𝑐𝑖𝑡 , 𝐷𝑐𝑖𝑡 , and 𝐷𝑐𝑖𝑡 , which take the value of 1 if month t falls before move-in for individual i, within 0–5 months after move-in, within 6–11 months after move-in, and more than one year after move-in. We expect that 𝛾 bef = 0 because the individual has not yet met his or her prospective neighbors. Therefore, we use this as a placebo test. If the peer effect exists, 𝛾 0_5 is expected to be positive; 𝛾 6_12 and 𝛾 1yr can also be positive, but are expected to be smaller than 𝛾 0_5 for the following two reasons. First, since peerci is measured around move-in, the difference between peerci and employment rate among peers in month t increases over time. Given that individuals’ employment probability at period t is expected to be influenced 19 Previous studies estimate the impact of the peers’ labor market outcome on the outcome of respondents during a certain period, such as the period of the household survey (Damm, 2009, 2014; Edin et al., 2003). Nevertheless, we employed a hazard model to exploit information about when respondents restarted work. Furthermore, since the duration between the time of move-in and the survey period shows large variation among respondents, regressing the survey date employment status of peerci would yield imprecise and hard-to-interpret estimation results. 20 If we limited our sample to those who did not start work before move-in and set the month of move-in as the starting point, the remaining sample would be non-randomly selected. We thank Daniel Hamermesh for pointing out this issue. We also estimate the model using a left-censored sample. The result, which is qualitatively the same, is available upon request from the corresponding author.

A. Kondo and M. Shoji

by the peer employment rate of that period, peerci likely becomes less relevant as the gap between peerci and the contemporaneous peer employment rate widens. Second, if the peer effect is heterogeneous across individuals, those who are affected by peers should find a job quickly and exit the sample, especially when peerci is high. Thus, those who remain in the sample after six months are likely to be less responsive to the peer employment rate. We also allow the baseline hazard, 𝜆(t; sexci ), to vary by gender, because the survival functions shown in Fig. 4 are quite different between men and women. The vector of control variables, Xci , in the exponential part includes dummies for 10-year age categories, dummies for educational background, household size, dummies for the level of housing loss, an indicator for any loss of household members due to the tsunami or earthquake, and dummies for 0–5 months after move-in, 6–11 months after move-in, and more than one year after move-in. 𝜃 c represents housing cluster fixed effects. Standard errors are clustered at the housing cluster level to allow any unobservable, time-variant common shock to apply to all households in the same housing cluster.21 The variables included in Xci and the cluster fixed effect 𝜃 c also serve as controls for financial compensation from TEPCO. As mentioned in Section 2.3, monthly compensation for mental distress is supposed to be paid until the evacuation order is lifted. Thus, the expected time when this compensation is canceled depends on the resident municipality before the accident, which is controlled through cluster fixed effects. The compensation for foregone income is determined by the income from the job lost due to the power plant accident. Although we do not have a direct measure of pre-accident income, we control for human capital variables, such as age, education, gender, and work industry before the accident. It is worth emphasizing that, thanks to the random assignment of peers, the amount of compensation must be uncorrelated with the peer employment rate even without these controls, while the amount of compensation may have directly affected the individual’s labor supply. As Manski (1993, 2000) points out, in general settings, it is difficult to estimate the causal effect of the behaviors of an individual’s peers because self-sorting or common shocks could generate a spurious correlation between an individual’s and his or her peers’ behaviors. That is, individuals in the same group tend to behave in the same way because they have similar individual characteristics or face similar conditions. We solve the problem of self-sorting by exploiting the random assignment of housing locations by lottery. Although the selection into housing clusters is not random, this non-random sorting to each housing cluster is controlled by housing cluster fixed effects. In addition, the assignment within a cluster is random. Moreover, our estimates were not affected by common shocks because the employment status of peers at the time of move-in should be uncorrelated with any block-level shocks that might occur after movein. Furthermore, thanks to the lottery, individuals currently living in the same block were unlikely to have experienced any common shocks before move-in because they were randomly chosen from more than 100 temporary shelters and they did not know each other until moving into the housing. Finally, by using the employment status of peers determined before they moved in as the main explanatory variable, we can also avoid the problem of simultaneity, or the reflection problem. The key assumption for our identification strategy is that the assignment of temporary housing was actually random. Random assignment of housing, with the characteristics of the housing clusters being constant, predicts that peers’ employment status should be independent of individual characteristics. To confirm this, we used a sample of those who were not working as of the end of March 2011 to regress the neighbors’ employment rate on the individual characteristics and the housing cluster fixed effects. Table 5 shows the results. Columns (1) and (2) present estimates both without and with control for the work industry before the

21 Note that this also allows for autocorrelation of error terms at the individual level since no individuals in our sample moved across housing clusters.

Journal of Urban Economics 113 (2019) 103195

power plant accident and the gap between the completion of construction and move-in, respectively. None of the coefficients is statistically significant and joint tests of significance for age dummies, education dummies, housing loss dummies, and dummies for the work industry before the accident are insignificant. The insignificance of the timing of move-in implies that random assignment applied not only for those who moved in immediately after the completion of construction but also for those who moved in later. Further, given the large coefficient of having a university degree in columns (1) and (2), we additionally controlled for interaction terms between gender and education categories in column (3). The result does not change qualitatively, although the industries of work become marginally significant using a joint significance test (pvalue = 0.07). These results provide evidence of the randomness of the assignment of peers within housing clusters. 5. Results 5.1. Baseline result Table 6 shows the estimated coefficients of the hazard model (1). Full estimation results are reported in Appendix Table A1. Column (1) controls only for cluster and period fixed effects, and column (2) further includes basic demographic background characteristics, such as age, educational background, household size, dummies for housing loss, and an indicator for the loss of any household members. In column (3), we add work industry dummies before the power plant accident. The results are almost the same. As expected, peerci does not have any effect on hazard before move-in to the temporary housing, which implies that there is no within-block correlation caused by self-sorting or common shocks at the block level. In contrast, there is a statistically significant positive peer effect in the first six months after move-in. After the first six months, the effect fades. To interpret the estimated 𝛾, recall that when peerci increases from a to a + b, the right-hand side of Eq. (1) becomes exp(𝛾b) times larger. The estimated coefficient in column (3) implies that an increase of one percentage point in peerci would make the hazard of restarting work exp(2.164 × 0.01) = 1.02 times larger during the first six months. Since the standard deviation of peerci is 0.16, a one standarddeviation increase in peerci would make the hazard of restarting work exp(2.164 × 0.16) = 1.41 times larger. For the sake of comparison with existing studies, we convert this estimate into the effect of a one percentage-point increase in peer employment rate on an individual’s own employment rate as follows. The average hazard (probability of finding a job in each period) in the first six months after move-in is 1.9%, and a one percentage-point increase in peerci raises this to 1.9% × exp(2.164 × 0.01) = 1.94%. Thus, the change in the employment rate after the first six months since move-in should be (1−0.019)6 −(1−0.0194)6 = 0.0022. This means that a one percentagepoint increase in the peer employment rate leads to a 0.22 percentage point-increase in an individual’s own employment probability. This is smaller than the effect estimated by Maurin and Moschion (2009), who find that a one percentage-point increase in a neighbor’s labor market participation among French women aged 21–35 years increased one’s own labor market participation by about 0.6 percentage points. Although only a few of the other variables are statistically significant, the signs of the estimated coefficients are reasonable. Individuals older than 60 years of age are less likely to start working, whuch probably reflects the lack of employment opportunities available to them. The difference across educational backgrounds is negligible. Household size, level of housing loss, and loss of household members also seem to have negligible effects. Those who had no job before the accident (the reference group for work industry before the accident) are significantly less likely to restart work. Appendices A2–A4 present robustness checks. In Appendix A2, we address concerns about the peer effect of members of other blocks, although the omission of this effect should cause a downward bias, as

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Journal of Urban Economics 113 (2019) 103195

Table 5 Test for exogeneity of neighbors’ employment status. Dependent variable: Percentage of neighbors who had started working before moving into temporary housing.

Male Age 30–39 years Age 40–49 years Age 50–59 years Age 60–69 years High school Vocational/Jr college University

(1)

(2)

(3)

−0.009 [0.010] −0.020 [0.034] 0.040 [0.032] −0.004 [0.027] 0.005 [0.027] −0.001 [0.015] −0.011 [0.033] 0.036 [0.048]

−0.011 [0.007] −0.024 [0.037] 0.035 [0.032] −0.009 [0.030] 0.002 [0.028] 0.001 [0.015] −0.014 [0.034] 0.029 [0.043]

0.003 [0.004] −0.016 [0.012] 0.001 [0.034] −0.007 [0.035] −0.009 [0.031]

0.003 [0.004] −0.016 [0.014] 0.000 [0.032] −0.008 [0.035] −0.012 [0.032] 0.008 [0.031] 0.020 [0.029] 0.024 [0.042] −0.006 [0.018] 0.036 [0.023] 0.001 [0.021] −0.001 [0.002]

0.012 [0.017] −0.024 [0.037] 0.037 [0.032] −0.007 [0.027] 0.004 [0.028] 0.017 [0.023] 0.000 [0.029] −0.023 [0.120] −0.034 [0.023] −0.028 [0.022] 0.058 [0.108] 0.003 [0.004] −0.017 [0.014] 0.000 [0.032] −0.010 [0.034] −0.010 [0.032] 0.013 [0.034] 0.019 [0.029] 0.024 [0.041] −0.007 [0.018] 0.039 [0.024] 0.003 [0.022] −0.001 [0.001]

0.28 0.46 0.50 –

0.30 0.21 0.60 0.11

0.37 0.28 0.62 0.07

479 0.231

477 0.236

477 0.240

High school x Male Vocational/Jr college x Male University x Male Household size Housing loss: partial Housing loss: half Housing loss: full Dummy for having lost household member(s) by the tsunami Work industry before the accident: agriculture and fishery Work industry before the accident: construction/utility Work industry before the accident: manufacturing Work industry before the accident: sales and service Work industry before the accident: medical Work industry before the accident: other Gap between construction completion and move-in P-values of F-test for joint significance Age dummies Education dummies Housing loss dummies Work industry before the accident Observations R-squared

p < 0.01, ∗ ∗ p < 0.05, ∗ p < 0.1. Housing cluster fixed effects are included. Standard errors clustered at the housing cluster are in brackets. The sample size is smaller in column (2) because two individuals did not answer for work industry before the accident. ∗∗∗

discussed in Section 2.2. Appendix A3 presents seven robustness tests for different sample restrictions. First, we exclude those participants who were not working before the accident (mainly women). Second, as argued in Section 2.3, the labor demand in the construction and utility industries significantly increased after the accident. We therefore exclude those who worked in these industries before the accident to mitigate the effect of specific labor market conditions. Third, we limit the sample to those who moved in within two months following the completion of the housing cluster to confirm that our results were not driven by people who moved in later. Fourth, we also estimate the model using the subsample of survey respondents, given the possibility of measurement

errors in the non-respondents’ information. Fifth, we exclude individuals from the cluster in which the timing of application for housings may differ across residents (Minamidai cluster). Sixth, we exclude samples from municipalities where sample selection due to relocation from temporary housing may be serious. Seventh, we estimate the model without the samples of evacuees who lost their family members in the disaster. Finally, in Appendix A4, we additionally control for peers’ predetermined characteristics, such as work experience and educational status, in order to test whether the results were driven by peers’ employment status or their characteristics. Our main results are robust to all of these alternative samples.

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Table 6 Effects on the hazard of restarting work.

Percentage of neighbors who had restarted work before moving into temporary housing (peerci ) × before move-in × 0–5 months after move-in × 6–11 months after move-in × more than 1 year after move-in Control for Control for Number of Number of

work industry before the accident age, education, household size, disaster damage observations individuals

(1)

(2)

(3)

0.153 [1.479] 2.497∗ ∗ [1.063] 0.366 [0.911] 0.081 [1.218]

0.265 [1.608] 2.665∗ ∗ [1.041] 0.799 [0.938] 0.458 [1.210]

−0.308 [1.513] 2.164∗ ∗ [0.870] 0.648 [0.944] 0.485 [1.259]

No No 10,942 479

No Yes 10,942 479

Yes Yes 10,906 477

Full estimation results are reported in Appendix Table A1. The mean dependent variable (average rate of restarting work per month conditional on not having restarted work) is 0.016. ∗ ∗ ∗ p < 0.01, ∗ ∗ p < 0.05, ∗ p < 0.1. Standard errors clustered at the housing cluster are in brackets. Both specifications include controls for housing cluster fixed effects and dummies for 0–5 months after move-in, 6–11 months after move-in, and more than 1 year after move-in. The sample size is smaller in column (2) because two individuals did not answer for work industry before the accident.

5.2. Heterogeneous effect across age and educational background In this subsection, we examine whether the peer effect is heterogeneous across age and educational background. In particular, people older than 60 years may behave differently, given that many people start to consider retirement after age 60. It is also policy-relevant since about half of the adult evacuees living in temporary housing are older than age 60. Regarding educational background, as summarized in Ioannides and Loury (2004), existing studies on network and referral in job searches show that high school graduates rely on neighborhood networks more than college graduates. Table 7 shows the estimated coefficients of the interaction terms between peerci and dummy variables for being older than age 60 and for being vocational or university graduates. First, columns (1) and (2) show that the peer effect has a statistically significant positive impact for those with a high school or lower education level. This result is consistent with previous studies on network and referral effects. However, note that the point estimate of the effect in the first six months for the more educated group is also positive, though insignificant and only half as large as that of the less educated group. Given the smaller sample size of the more educated group, we cannot conclude whether the peer effect exists for individuals with vocational or with college education. Second, columns (3) and (4) of Table 7 show that the peer effect has a statistically significant positive impact only for those younger than age 60. Although the interaction term between peerci and dummy variables for being older than 60 years is not statistically significant, the point estimate indicates that peerci has a negative effect on the job-restarting hazard even for those older than age 60. 5.3. Role of gender Since traditional gender roles impose more pressure to work on men than on women, one may think that the peer effects are stronger within than across genders. Thus, this subsection computes the employment rate of male and female peers separately to examine the heterogeneity of the peer effect relative to own and peers’ gender. Specifically, let peerm ci and peerf ci denote the employment rate of male and female peers in the same block (excluding those living in the same housing unit), respectively. Then, we replace peerci in Eq. (1) with the following four interaction terms: peerm ci × maleci , peerf ci × maleci , peerm ci × femaleci , and peerf ci × femaleci . When interpreting the result, however, we need to keep in mind that the sampling errors in the observed peerm ci and peerf ci are substantial.

Recall that our data is a 50% sample of all residents, thus peerci defined without regard to gender already includes substantial sampling errors. Specifically, the average number of working-age adults living in the same block (excluding those living in the same housing unit) is 15.7, thus a change in the employment status of one of the peers moves peerci by 6 percentage points. When we divide the sample by gender, the average number of peers in the sample halves: 8.0 for men and 7.7 for women. This means that a change in the employment status of one of the male peers moves peerm ci by 13 percentage points. Since the sampling errors in peerm ci and peerf ci are larger than those included in peerci , the estimated coefficients of peerm ci and peerf ci are not directly comparable to that of peerci . Moreover, peerf ci takes zero too often: 38.6% of our sample have no female peers working at the time of move-in. Appendix Tables A7 and A8 present the detailed summary statistics of peerm ci and peerf ci and the balancing test, respectively. Keeping these limitations in mind, columns (1) and (2) of Table 8 present the estimation results. The effects for the male sample appear to be reasonable: statistically significant positive effects from male peers in the first 6 months after move-in, although smaller than those in the main specification probably because of the attenuation bias due to sampling errors, and insignificant effects from female peers. However, the estimated effects for the female sample are difficult to interpret; statistically significant positive effects from male peers and significantly negative effects from female peers, both in the first 6 months after movein. In particular, the negative coefficient of female peers is counterintuitive. There are two potential explanations for this result. First, the result could be driven by sampling errors from outliers. Since only 8% of women restarted work before move-in, the result of female peers is more sensitive to outliers than that of male peers. Second, the employed female peers may bring discouraging information about jobs available for women. The demand for female workers was concentrated to care workers in elderly care facilities, and such “female jobs” are, on average, more stressful but paid much lower than “male jobs” such as construction. If the second channel drives our result, we should observe even larger negative peer effects for disadvantaged evacuees, such as older evacuees with no work experience, for whom better jobs are unlikely to be available. Hence, we estimate the same model using the sample of those aged over 50 and those who were not working before the accident. Columns (3) and (4) present the result. Counter to the prediction of the second channel, the employment rate of both male and female peers do not have significant effects on female evacuees. Therefore, we interpret that the observed peer effects in Table 6 are driven by male evacuees.

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Journal of Urban Economics 113 (2019) 103195

Table 7 Heterogeneous effects. Coefficient of percentage of neighbors who had restarted work before moving into temporary housing (peerci ) interacted with:

(1)

(2)

High school or less × before move-in High school or less × 0–5 months after move-in High school or less × 6–11 months after move-in High school or less × more than 1 year after move-in Vocational/Jr college/University × before move-in Vocational/Jr college/University × 0–5 months after move-in Vocational/Jr college/University × 6–11 months after move-in Vocational/Jr college/University × more than 1 year after move-in Younger than age 60 × before move-in Younger than age 60 × 0–5 months after move-in Younger than age 60 × 6–11 months after move-in Younger than age 60 × more than 1 year after move-in 60 years or older × before move-in 60 years or older × 0–5 months after move-in 60 years or older × 6–11 months after move-in 60 years or older × more than 1 year after move-in

0.980 [1.435] 3.047∗ ∗ ∗ [0.989] 0.878 [1.382] 0.704 [1.128] −1.516 [1.949] 1.278 [1.705] 0.258 [1.279] −1.055 [2.151]

0.563 [1.254] 2.778∗ ∗ ∗ [0.878] 0.919 [1.325] 0.906 [1.258] −2.566 [2.012] 0.173 [1.481] −0.099 [1.451] −1.410 [2.126]

(3)

(4)

1.185 [1.209] 3.759∗ ∗ ∗ [0.907] 1.900∗ ∗ [0.958] 1.752 [1.336] −1.604 [2.314] −1.160 [1.988] −2.114 [1.899] −1.809 [1.946]

0.640 [1.149] 3.172∗ ∗ ∗ [0.726] 1.628 [1.098] 1.695 [1.427] −2.276 [2.327] −1.792 [2.074] −2.367 [1.965] −2.013 [2.029]

Control for work industry before the accident Number of observations Number of individuals

no

yes

no

yes

10,942 479

10,906 477

10,942 479

10,906 477

p < 0.01, ∗ ∗ p < 0.05, ∗ p < 0.1. Standard errors clustered at the housing cluster are in brackets. Both specifications include the same explanatory variables as in Table 6. ∗∗∗

6. Discussion: potential underlying mechanisms There are three potential channels driving the peer effect in employment: joint consumption, the social norm to work, and residence-based job information networks. First, to join in with the leisure activities undertaken by neighbors with decent jobs, one would need as much income as those neighbors. Thus, unemployed individuals may try to restart work in order to join in with the activities. Second, a social norm to work could make unemployed evacuees feel uncomfortable when others in the same block have jobs. Such pressure may make more evacuees resume work. Third, neighbors may provide useful information for job searchers. These residence-based job information networks include both direct referrals from the neighbor’s employers and general information sharing.22 The first channel is testable with our data. If peer effects in employment are driven by joint consumption, we should find a positive im-

22 First, the neighbors may bring direct referrals to their employers (Montgomery, 1991). Hellerstein et al. (2011) and Schmutte (2015) show that neighbors are more likely to work in the same establishments. Second, employed workers may pass on information about job vacancies that they did not take (Calvó -Armengol and Jackson, 2007). As evidence for this channel, Schmutte (2015) shows that the positive correlation in earnings among neighbors remains after dropping those likely to have been hired through direct referrals.

pact of the peer employment rate on household expenditure for food and leisure activities. Our survey collected information on the extent to which these expenditures changed between the move-in and survey periods. The possible answers range from one (decreased by more than 50%) to nine (increased by more than 50%). Using the sample of those who were unemployed at the time of move-in, we regress these indicators on peer employment rate, female dummy, and the other controls included in the hazard model. Columns (1) and (2) of Table 9 present the estimation result of an ordered probit model. The coefficient of peer employment rate is statistically insignificant, ruling out the possibility of joint consumption. Next, as suggestive evidence for the second channel, we test whether social norms play an important role by examining the impact of the peer employment rate on the subjective well-being of the initially unemployed evacuees. The idea is as follows. A social norm to work could make those who have not yet started to work feel less comfortable when more neighbors are working. On the contrary, the impact on those able to find jobs after the move-in is expected to be zero. So if the social norm to work drives the peer effect, the employment rate among an individual’s peers will have a non-positive effect on his or her subjective well-being. By contrast, residence-based job information networks will not produce such an effect on subjective well-being. If there is any effect, the peers’ employment rate should have a positive effect on those who found a job after move-in. This is because more information gained through employed peers enables the unemployed to find better jobs,

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Journal of Urban Economics 113 (2019) 103195

Table 8 Effects of employment rates of neighbors by gender. Sample:

Full

Over 50 or Unemployed before the accident

(1)

(2)

(3)

(4)

peerm ci × male × before move-in peerm ci × male × 0–5 months after move-in peerm ci × male × 6–11 months after move-in peerm ci × male × more than 1 year after move-in peerf ci × male × before move-in peerf ci × male × 0–5 months after move-in peerf ci × male × 6–11 months after move-in peerf ci × male × more than 1 year after move-in peerm ci × female × before move-in peerm ci × female × 0–5 months after move-in peerm ci × female × 6–11 months after move-in peerm ci × female × more than 1 year after move-in peerf ci × female × before move-in peerf ci × female × 0–5 months after move-in peerf ci × female × 6–11 months after move-in peerf ci × female × more than 1 year after move-in

0.503 [0.833] 1.791∗ ∗ [0.802] −0.726 [1.320] 0.114 [1.107] −0.058 [1.412] 0.253 [1.290] 1.524 [2.761] 3.954∗ [2.078] −0.361 [1.049] 2.026∗ ∗ ∗ [0.738] 0.128 [0.611] −0.567 [0.975] −2.684 [2.706] −1.998∗ ∗ ∗ [0.741] 1.549 [1.874] 0.030 [2.157]

0.282 [0.776] 1.569∗ ∗ [0.697] −0.468 [1.352] 0.626 [1.317] 0.269 [1.344] 0.622 [1.432] 1.718 [2.549] 3.695 [2.329] −0.533 [1.017] 1.778∗ ∗ ∗ [0.689] 0.206 [0.763] −0.475 [1.097] −3.638 [2.874] −3.437∗ ∗ ∗ [1.026] 0.446 [2.281] −0.947 [2.150]

0.436 [1.002] 2.410∗ ∗ [1.113] −3.884 [2.820] 1.604 [1.431] −2.037 [1.374] −1.303 [1.954] 4.361 [5.169] 3.593 [3.184] −0.816 [1.735] 0.315 [1.506] −1.862 [1.441] 0.281 [0.495] −7.552 [5.626] −0.282 [1.255] 2.021 [3.564] −3.812 [3.501]

0.985 [1.134] 2.952∗ ∗ [1.177] −3.214 [3.032] 2.328 [1.761] −1.666 [1.236] −0.732 [2.196] 4.086 [5.437] 3.875 [3.481] −1.212 [1.845] −0.204 [1.396] −2.212 [1.580] 0.068 [0.691] −8.303 [5.547] −0.745 [1.767] 1.297 [4.767] −4.927 [3.737]

Control for work industry before the accident Number of observations Number of individuals

no 10,740 470

yes 10,704 468

no 8257 336

yes 8227 335

p < 0.01, ∗ ∗ p < 0.05, ∗ p < 0.1. Standard errors clustered at the housing cluster are in brackets. Both specifications include the same explanatory variables as in Table 6. ∗∗∗

while the impact on those who remain unemployed is zero.23 Hence, in the absence of peer pressure from the social norm to work, the effect of peer employment rate on subjective well-being should be non-negative. As proxies for subjective well-being, our dataset includes three measures of happiness. The first measure is happiness compared with other evacuees in the cluster, which is elicited by asking the following question: “Do you think you are happier than the other evacuees in the same cluster?”24 Second, we measure happiness compared with the evacuees in the other clusters with the following question: “Do you think you are happier than the evacuees in the other clusters?” Third, we asked a

23 An anonymous reviewer pointed out that, compared with jobs found through formal job searches, jobs found through networks are associated with a worse job-worker match, as suggested by their lower wages and shorter job duration (Loury, 2006). Yet, we believe it is reasonable to assume that taking a job found through an informal job search would be better than being unemployed. Thus, unless informal job searches crowd out formal job searches, which is unlikely, information sharing or the referral effect will not produce a negative effect of the peer employment rate on subjective well-being. 24 Unlike the standard questionnaire design used in the literature, we employ relative happiness compared with other evacuees in the same cluster for three reasons. First, we believe our question clearly captures the effects of the disparity in employment status within a cluster. Second, if we employed the standard question, we can easily expect that most, if not all, respondents would select the lowest score, given their current socioeconomic and emotional situation. Therefore, we would not observe enough variation. Finally, we believe that it is against research ethics to ask respondents—who have obviously experienced one of the worst hardships of their lives—to what extent they feel happy.

similar question to measure the change in happiness since moving into the temporary housing. The possible answers range from one (strongly disagree) to seven (strongly agree) for all questions. These variables are available only for the respondent of each surveyed household. Among these, however, we do not use the third measure, because the impact of the peer employment rate on it is theoretically ambiguous. A drawback of the first measure is that even without social norms, an individual who wishes to work but cannot find a job may feel less happy than the other evacuees if they are working. The second measure partially mitigates this issue because the reference point in this measure differs from the respondent’s peer group. Nonetheless, this measure could still face the same issue if the respondent infers the living standard of the evacuees in the other clusters from his or her neighbors in the same cluster. Hence, we consider our results as suggestive evidence. Columns (3) to (6) of Table 9 report the result of the ordered probit model using the sample of those who were unemployed at the time of move-in. The sample size is smaller than in columns (1) and (2) since happiness measures were elicited only from survey respondents. Columns (3) and (5) present the overall effect of the peer employment rate on the two happiness measures. The significantly negative coefficients of the peer employment rate are consistent with the prediction by social norm to work. Columns (4) and (6) present a model allowing the effect to vary based on whether the individual has restarted to work by the time of survey. This specification is motivated by the prediction that peer pressure makes those who have not yet started to work feel unhappy, while the impact of peer employment rate on those who have already started

A. Kondo and M. Shoji

Journal of Urban Economics 113 (2019) 103195

Table 9 Test for underlying mechanisms of peer effects.

peerci

Expenditure for

Happiness compared to

Food

leisure

other evacuees in the same cluster

the evacuees in the other clusters

(1)

(2)

(3)

(5)

0.196 [0.490]

0.089 [0.690]

(4) ∗∗

−0.724 [0.305]

peerci × restarted job by the time of survey

Restarted job by the time of survey Control for work industry before the accident Number of individuals

−0.884 [0.321] −2.679 [1.679] −0.555∗ ∗ [0.279] 0.718 [0.605]

peerci × not restarted job by the time of survey

Yes 393

yes 393

yes 226

(6) ∗∗∗

yes 226

−0.849 [1.392] −0.867∗ ∗ ∗ [0.296] −0.204 [0.441] yes 226

yes 226

Note: Change in food and leisure expenditure since move-in is measured on a 1–9 scale (1: decreased by more than 50%, 2: decreased by 30–50%, 3: decreased by 10–30%, 4: decreased by less than 10%, 5: same as before, 6: increased by less than 10%, 7: increased by 10–30%, 8: increased by 30–50%, 9: increased more than 50%). Happiness is measured on a 1–7 scale. The coefficients of ordered probit model are reported. ∗ ∗ ∗ p < 0.01, ∗∗ p < 0.05, ∗ p < 0.1. Standard errors clustered at the housing cluster are in brackets. Other explanatory variables are the same as those in Table 6 and the female dummy. The sample of those who were unemployed at the time of move-in is used. The sample size is smaller in columns (3) to (6), since happiness measures were elicited only from survey respondents.

to work is expected to be zero. Both columns show the impact of peer employment rate is significantly negative for those who remained unemployed, in line with the social norm hypothesis. However, although the large standard errors make the estimated coefficients statistically insignificant, the impact for those who restarted a job after move-in is also negative: the point estimate is even larger (column [4]) or comparable (column [6]) with that of unemployed evacuees. Nonetheless, since the residence-based job information networks predict a positive coefficient, they cannot explain this pattern either. Furthermore, employment status at the time of the survey itself is endogenous to the peer employment rate at the time of move-in. Since our data do not allow us to address this issue rigorously, we prefer the specification without the interaction with the employment status at the time of survey, presented in columns (3) and (5). While our results may not be conclusive, taken together, given that the impact for the employed is statistically insignificant and not positive, we consider these results as supporting evidence for the social norm hypothesis. Our finding is consistent with field interviews conducted by the authors with evacuees who accused other evacuees of not working. It is also in line with (Stutzer and Lalive’s 2004) findings that a social norm to work in a geographically defined local community shortens the duration of unemployment. In addition, thanks to high labor demand, evacuees can find a job relatively easily as long as they are willing. Indeed, most evacuees did not have prolonged job searches: among 174 individuals who restarted work between April 2011 and September 2013, 149 did so within three months after beginning to search. These circumstances could potentially strengthen the peer effect driven by peer pressure against those not working. Finally, given the lack of information about evacuees’ current jobs, it is difficult to investigate the role of residence-based job information networks. If we knew whether the respondents tended to start working in the same occupation as their peers, we could test the existence of direct referrals.25 Alternatively, if we were able to estimate the effect of peerci on current earnings, we could obtain suggestive evidence for the residence-based job networks, because both direct referrals and information sharing are expected to improve match quality (Dustmann et al., 2016; Calvó-Armengol and Jackson 2007). Unfortunately, as explained

25 For example, we could compare whether a pair of neighbors in the same block are more likely to work in the same kind of job than a pair from the same cluster but different block.

in Section 3.2, we were not able to ask these questions for fear of offending the respondents. That said, we speculate that both channels may have contributed to some extent. Given the high vacancy rate in the Iwaki area, some employers may have had to rely on the referrals through their employees to fill positions. Also, many evacuees were unfamiliar with the job opportunities in Iwaki city when they moved into temporary housing, information from other evacuees who had already found jobs in Iwaki may have played an important role in their job search. At the same time, the role of these informal job search may not be as important for the evacuees in our sample as for the refugee immigrants studied by Edin et al. (2003) and Damm (2009, 2014), because the evacuees have good access to formal job search channels.

7. Conclusion In this study, we exploited the random assignment of temporary housing for evacuees from the Fukushima Daiichi nuclear power plant accident to identify the effect of their neighbors’ employment rate on their probability of finding a job after evacuation. While controlling for housing cluster fixed effects, the assignment of blocks within each housing cluster was found to be completely random, and this enabled us to identify the causal effect of neighbors’ employment status on each resident’s probability of finding a job for him or herself. We found a significantly positive peer effect that is robust to controls for various individual-level characteristics and different sample restrictions. Not only was the effect statistically significant, but its size was substantial: a one standard-deviation increase in the peer employment rate increases the hazard of restarting work by 1.41 times in the first six months after move-in. In addition, we find suggestive evidence consistent with the hypothesis that the observed peer effect is caused by the social norm that everyone should work, although we cannot completely disentangle all the potential mechanisms given data limitations. Natural disasters and civil conflicts often force people in affected areas to migrate and form new communities. Our results imply that the members of the new community to which migrants are assigned can substantially affect his or her economic outcomes. Evacuees and refugees are influenced more by their peer evacuees or refugees than by local neighbors, who are often economically more advantaged. Furthermore, we provide evidence for a positive peer effect even when the financial incentive to work is low. Our results suggest that social norms play an important role; perhaps the low financial incentive enhanced intrinsic

A. Kondo and M. Shoji

motivation for normative behavior and strengthened the social pressure to work. Our findings also provide some useful insights into post-disaster rehabilitation policy. First, the significant positive peer effect suggests that social interactions with employed individuals can significantly facilitate reemployment. In particular, segregating unemployed evacuees could impede recovery. Second, ignoring the spillover effect might lead to under-evaluation of the effectiveness of policies to promote employment of evacuees. Third, even if each cluster of evacuees is ex ante homogenous, peer effects may generate persistent disparities across clusters by amplifying random shocks to each cluster. Fourth, the findings on social norms imply that fostering social capital may enhance resilience against natural disasters. Acknowledgement Japan Society for the Promotion of Science KAKENHI Grants Number 25780172 (PI: Masahiro Shoji) and 15K17072 (PI: Ayako Kondo) supported this research. The authors are grateful to the Iwaki Liaison Council to Support the Disaster-Victims of 3.11 for their valuable cooperation in the household survey. We also thank David Neumark, the editor, and three anonymous reviewers, Drew Griffen, Daniel Hamermesh, Shin Kanaya, Ryo Nakajima, Koyo Miyoshi, Eric Weese, seminar participants at the 8th Trans Pacific Labor Seminar, the 11th World Congress of the Econometric Society, the 21st Annual Meeting of Society of Labor Economists (SOLE), the 30th European Society for Population Economics conference, The University of Tokyo, Hitotsubashi University, the Workshop on Natural Disasters, the Kyoto Summer Workshop on Applied Economics, Hitotsubashi Summer Institute on Labor Economics, the National Institute of Population and Social Security Research, Tohoku University, University of Tsukuba, and Otaru University of Commerce for many constructive suggestions. The authors obtained IRB approval for this project from Seijo University IRB. Supplementary materials Supplementary material associated with this article can be found, in the online version, at doi:10.1016/j.jue.2019.103195. References Barnhardt, S., Field, E., Pande, R., 2015. Moving to opportunity or isolation? Network effects of a randomized housing lottery in urban India. Am. Econ. J. 9 (1), 1–32 forthcoming. Bayer, P., Ross, S.L., Topa, G., 2008. Place of work and place of residence: informal hiring networks and labor market outcomes. J. Pol. Econ. 116 (6), 1150–1196. Benabou, R., Tirole, J., 2000. Self-Confidence and Social Interactions, p. 7585 NBER Working Paper.

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