WPS3805 Di Bao: A Guaranteed Minimum Income in China's Cities? Shaohua Chen, Martin Ravallion1 Development Research Group, World Bank and Youjuan Wang National Bureau of Statistics, China Abstract: Concerns about incentives and targeting naturally arise when cash transfers are used to fight poverty. We address these concerns in the context of China's Di Bao program, which uses means-tested transfers to try to assure that no registered urban resident has an income below a stipulated "poverty line." There is little sign in the data of poverty traps due to high benefit withdrawal rates. Targeting performance is excellent by various measures; indeed, Di Bao appears to be better targeted than any other program in the developing world. However, all but one measure of targeting is found to be uninformative, or even deceptive, about impacts on poverty. We find that the majority of the poor are not receiving help, even with a generous allowance for measurement errors. While on paper, Di Bao would eliminate urban poverty, it falls well short of that ideal in practice. Keywords: Urban poverty, cash transfers, behavioral responses, targeting, China JEL: I38, O15 World Bank Policy Research Working Paper 3805, January 2006 The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the view of the World Bank, its Executive Directors, or the countries they represent. Policy Research Working Papers are available online at http://econ.worldbank.org. 1 For helpful discussions on this topic and comments on this paper the authors are grateful to Shubham Chaudhuri, Ren Mu, Philip O'Keefe, Xiaoqing Yu and staff of the Ministry of Civil Affairs, Government of China. 1. Introduction While economic reforms and structural changes in the Chinese economy have meant high rates of economic growth, it is believed that certain sub-groups have been adversely affected or have been unable to participate in the new economic opportunities due to their lack of skills, long-term illness or disability. The collapse of the old safety-net provided by guaranteed employment has left some households vulnerable. Some of the "left behind" households started poor and some became poor, even though aggregate poverty rates have tended to fall over time.2 Urban areas have figured prominently in these concerns about the "new poor." The "Minimum Livelihood Guarantee Scheme," popularly known as Di Bao (DB), has been the government's main response to this new challenge.3 The scheme started in Shanghai in 1993, then becoming a national policy with formal regulations issued by the State Council in 1999. (Here we are only concerned with urban DB; a rural version of the program is planned and has started in some provinces.) The program expanded rapidly once it became national policy and by 2003 participation had leveled off at 22 million people, representing 6% of urban residents, at a cost of about 0.1% of GDP (O'Keefe, 2004). The scheme is administered by the Ministry of Civil Affairs (MoCA). Di Bao aims to provide a transfer to all registered urban households with incomes below a DB line set at the municipal level.4 The aim is to close the gap between the recipient's income 2 On China's progress against poverty since reforms began around 1980 see Ravallion and Chen (2005). 3 A useful overview of the Di Bao program in the context of overall social assistance policy in China can be found in O'Keefe (2004). 4 "Registered" urban residents are those with an official registration for urban residence. There are also non-registered urban residents, who are often recent migrants from rural areas. Although it is not an issue we have been able to address in this study, we would hypothesize that the fact that the program is confined to households with urban registration is constraining its ability to reduce urban poverty. In testing that hypothesis one would clearly have to consider the possible incentive effects on migration decisions. This is a topic for future research. 2 and the local DB line (hereafter the "DB gap"), so that a minimum income is guaranteed. However, very little is known about the performance of the program in reaching the poor, even though it is evidently one of the largest cash transfer programs in the developing world. On paper, the program eliminates poverty (at least by its own definition of who is poor). But how close does it come to this ideal in practice? This paper offers the first systematic assessment of Di Bao's performance, based on independently-collected household survey data. We use the program as a case study for addressing a number of long-standing concerns about how effective transfer programs are in reducing poverty in developing countries. We focus on two issues that have clouded inferences from past work. Firstly, the performance of a program such as Di Bao will depend in part on behavioral responses. Yet in assessing targeting performance and poverty impacts it is common practice to simply deduct transfers received from post-transfer income to estimate pre-transfer income. Here there are concerns that recipients' labor supply or private transfer receipts will fall in response to DB, such that the net income gains are lower than the actual money received. On paper, the design of DB implies high marginal tax rates, which suggests that there may be strong incentive effects, which could undermine the program's effectiveness against poverty. The literature on the design of such programs suggests that the benefit withdrawal rate (BWR) -- the amount by which the transfer payment falls for each extra unit of pre-transfer income -- should be positive, but less than one. For programs aiming to reduce poverty a BWR around one half is consistent with evidence on the relevant income elasticity of labor supply (Kanbur et al., 1995). Taken literally, DB's aim of exactly filling the poverty gaps implies a BWR that is too high. However, it should not be assumed that any program operates exactly the way it is designed. There are many ways that the local administrators can dampen the marginal tax rates to avoid 3 adverse incentive effects, such as by delaying the withdrawal of benefits when DB participants get a new job. There are reports from field work that this happens in practice (O'Keefe, 2004). Whether the incentive problems are a concern in reality is an empirical question. Secondly, there are concerns about how "targeting performance" has been assessed in past work.5 A large share of the attention of policy-makers has gone into achieving better targeting, in the sense of concentrating benefits on the poor, notably by avoiding leakage to the non-poor. Various measures of targeting have been used in past work, and these are typically interpreted as measures of a program's performance in "..directing benefits toward poorer members of the population" (Coady et al., 2004a, p.81). However, while it is widely agreed in this literature that the objective is to maximize the impact on poverty,6 it is far from clear that any of the prevailing targeting measures provide a useful indicator for that objective. Indeed, there can be no guarantee that better targeting by these measures will enhance a programs' impact on poverty.7 We consider a range of measures found in the literature, and explore their relevance to the performance of the DB program in achieving it objective of eliminating poverty. Another common problem in past methods of assessing targeting performance is that the survey-based income measure may not coincide with the income concept used for targeting, thus clouding inferences. We address this problem by assessing performance against alternative income concepts, including a new method by which an "income" proxy is calibrated to the program's observed assignment. 5 These two issues are not of course independent; incentives depend on how transfers are targeted; assessments of targeting need to take account of incentive effects. 6 See, for example, the discussion in Coady et al., (2004b, Chapter 2). 7 See, for example, the results of Ravallion and Datt (1995) and Murgai and Ravallion (2005). For overviews of the generic issues raised by this class of policies see Besley and Kanbur (1993), Cornia and Stewart (1995), van de Walle (1998) and Ravallion (2005). The discussion in van de Walle (1998) -- preceding Coady et al., (2004) by six years in the same journal -- would surely lead one to question the relevance of the targeting measures used in the latter paper. 4 After describing our data for China's 35 largest cities in section 2, we outline our model of program participation in section 3. We then look for evidence of behavioral responses in section 4. The targeting performance of DB and its impact on poverty are the subjects of section 5. Section 6 concludes. 2. Data We use China's Urban Household Short Survey (UHSS) for 2003/04. The UHSS was done by the Urban Household Survey Division of the National Bureau of Statistics (NBS) as a first step in constructing the (smaller) sample for the regular Urban Household Survey (UHS), which has a much longer questionnaire. We use the UHSS sample for the 35 largest cities, giving a total sample of 76,000, varying from 450 (in Shenzhen) to 12,000 (in Beijing). For these 35 cities, the definitions of geographic areas in the UHSS coincide with those for the DB lines and the entire data set has been cleaned by NBS staff and made available for this research.8 While the UHSS is a relatively short survey, it allows us to measure a fairly wide range of household characteristics. The survey also included household income, as obtained from a single question, "What is your household's total income?" (though respondents were also asked how much of their income came from wages). This is unlikely to give as accurate a measure of income as the UHS, which builds up its income aggregate from many questions. So we must expect measurement errors. Questions were added to the survey on subjective perceptions of welfare, namely a question on whether the respondent felt that the household's income was 8 Outside these 35 cities, the local DB lines are not coded or use different codes, and in many cases use different boundaries to the geographic areas used by UHSS. So it is not feasible to assign DB lines to households outside the 35-cities sample. A further problem is that the bulk of the UHSS data outside the 35 cities has not been cleaned and local-level NBS staff were still working on the data at the time of writing. However, we cleaned the data ourselves for incomes and DB receipts for the full sample. We provide selected results from the full sample in an Appendix. 5 adequate for their needs, and whether income was improving over time. And we added questions to the UHSS on DB participation and income received from DB, for the purpose of this paper. However, this only includes the cash transfer from DB. It appears that some local governments also provide non-monetary benefits to DB participants, such as health-care and schooling entitlements, and sometimes a discount for the cost of utilities (notably in the north). We do not have data on these extra DB benefits. The UHSS was done during 2003 and 2004. The surveys in Beijing, Fujian, Hainan provinces and Kunming (the capital city of Yunnan province) were finished in 2003 while all others finished in 2004. Another problem is that we do not have a municipal cost-of-living index. The DB lines may well reflect cost-of-living differences, but they will also reflect other variables, including local fiscal capacity. We will discuss the likely biases due to this problem. 3. Model of Di Bao participation In using survey data to assess targeted transfer programs it is generally assumed that the income as measured in the survey is the same income measure used in implementing the program. This is a questionable assumption from three points of view. Firstly, there must be a strong presumption that income is measured with error in any survey; there are the usual reporting errors, but on top of this there are the likely extra errors in using a single income question, as well as the fact that the survey was done after the program was assigned, so the survey-based income net of DB receipts may differ from the income observed at the time the program was assigned (after the checks made by local authorities). Secondly, potential participants face an incentive to misreport their incomes; possibly the survey-based incomes are more accurate. The DB program does not rely solely on self-reported incomes. Local authorities and neighborhood committees try to assure that recipients are 6 genuinely eligible, taking account of other factors such as financial assets, consumer durables and housing conditions. There is also a community-appeals process, which includes the posting of applicants' names in a public place for two weeks. The national guidelines say that DB recipients are expected to work on "community services;" this would help screen the poor, although it is unclear whether work requirements are enforced locally (O'Keefe, 2004). Field studies in a few specific locations have revealed some possible concerns about income miss- reporting; for example, there are reports from qualitative research in Dalian that some people deliberately under-reported their incomes to obtain assistance (Daoshun and Tuan, 2004). Thirdly, it is important to note that there is more than one way to measure "income." One source of differences between survey-based incomes and those used to target the program is the time period over which income is measured. Current income can differ from long-term income; a young well educated family may have low current income but be on a rising trajectory with good future prospects. Anecdotal evidence also suggests that local authorities may not measure current income the same way households would report their income. Based on informal interviews with DB participants in Liaoning, Hussain (2002) reports that local authorities would measure income for DB purposes as if the family was receiving all the benefits it was entitled too, ignoring the fact that the family was not in fact receiving those benefits. The upshot of these considerations is that the allocation of DB is determined by a latent income measure. We assume that the program is allocated according to an unobserved money- metric of welfare given by: lnYi =(lnYi) + Xi +i * (1) Here Y is the observed measure of income net of DB receipts, which can enter nonlinearly through a strictly increasing parametric function , X is a vector of other factors, which may also 7 reflect measurement error in the observed, survey-based, income and i is a normally distributed error term with zero mean and variance . A household is eligible for the program if (and only 2 if) Yi < Zi , which is the local DB line (depending on where household i lives). We assume that * any household who is deemed eligible for DB will accept the transfer. Define a dummy variable that takes the value Di = 1 if household i receives the program and Di = 0 if not. The probability of participating is then given by: Pr(Yi < Zi) = F[(lnZi -(lnYi) - Xi)/ ] * (2) where F is the standard normal distribution function. We can then use a probit to estimate the parameters of (1) (normalized by ). Notice that the probability of participation is a strictly increasing function of the expected value of the proportionate DB gap, E(lnZi /Yi ) . This * assumes that the program works the way it is intended to. A more general model would allow for a more complicated selection process, as would arise from differences in the power of individuals to affect their DB participation, independently of their income. However, it is not clear that one can identify any variable that would influence "power' independently of income, so the more general model is not empirically distinguishable from the above model. The X's in equation (1) should clearly include geographic effects, since location can influence living standards independently of other household characteristics, including income. The municipality is the obvious geographic unit. We allow a complete set of municipality effects by m-1 dummy variables for the m municipalities (each with its own DB line). However, the DB line is constant within municipalities, so we cannot identify the coefficient on lnZi (the inverse of ) in (2) separately to the geographic effects. The vector X includes variables related to the dwelling and the observable characteristics of the household. 8 The detailed estimates for the probits are in the Appendix; results are given there with and without the net income variable (which enters as a quadratic in log income), given the concerns about its endogeneity. (We return to this issue.) Controlling for household income per capita, we find that DB participation is more likely for larger households, living in smaller dwellings, who do not own their dwelling, have an "old style" toilet, are still using coal for cooking, have no heating, no computer, have a female head of household, have a disabled or sick head of household, or a head with little schooling or who works in services or social security/welfare, or a head who is retired, works at home, has been laid off or is unemployed. DB households have lower financial wealth, are more likely to feel that their income is "less than they need to make ends meet," are more likely to think that their income has improved, have a lower share of wages in income, have more unemployed or students in the household but fewer retired people. Most cities have significantly lower participation rates than Beijing, controlling for household characteristics. (Later we investigate the differences across cities.) It appears that the program is putting heavier weight on certain characteristics, such as poor dwelling attributes and lack of financial wealth, than is implicit in household income per person from the UHSS. To the extent that these effects reflect measurement errors in incomes or a broader concept of "income" that is motivating the program's targeting at local level, it can be argued that the program is doing a better job of reaching the poor than our calculations based solely on the survey-based incomes would suggest. We return to this point in section 5. There are also indications that the program is doing better at reaching the chronically poor than those who may be vulnerable to poverty in the future. This is suggested by the fact that people who feel that they are on a downward trajectory are less likely to get support from DB. 9 It is clear from the above results that DB participants are a highly selected sub-sample. The Appendix gives the frequency distribution of the probit's predicted probabilities ("propensity scores") according to whether the sampled household participated in DB. We find that the sample of non-participants is heavily skewed toward zero probability of participating in DB. There are clearly a great many households in the sample who have negligibly low probabilities of participating in the program. However, there is a region of common support, in that there are at least some non-participants with similar propensity scores to all the participants. 4. Behavioral responses One cannot assess a programs' targeting performance and impacts on poverty without taking a position on the behavioral responses to the program that influence the net income gains. However, assessing behavioral responses to a program such as DB without longitudinal (panel) data is difficult.9 With only a single cross-sectional survey it is hard to be confident in the results, given the likelihood of omitted variables correlated with both program placement and the behaviors of interest. However, it is still worth seeing whether there are indications in our data of behavioral responses to the program. The key thing we are looking for is any sign that the program had an impact on the incomes of participants net of the transfers they received. We use two approaches that can at least throw some light on whether there are likely to be significant behavioral responses relevant to our later assessment of targeting performance and impacts on poverty. First we estimate the marginal tax rate, to see if this is high enough to warrant concerns about behavioral impacts. Then we use a non-experimental evaluation method, which estimates impacts against a matched comparison group. 9 And even with longitudinal data there can be severe identification problems; for further discussion see Ravallion (2005b, sections 7 and 8). 10 4.1 Benefit withdrawal rate The design of DB intends that the benefits received will decrease as income rises, so that (in theory at least) participants face a positive marginal tax rate. Indeed, if DB exactly fills the gap between current non-DB income and the DB line (as is the scheme's aim) then participants will face no incentive to work. Earned income net of DB will fall to zero (assuming that work yields disutility). The program will have created a poverty trap, whereby participants do not face an incentive to raise their own incomes, because of the loss of benefits under DB. The extent to which this is a real problem in practice is unclear. Benefits are unlikely to be withdrawn quickly. There are reports that at least some local authorities allow DB benefits to continue for some period after the participant finds a job (O'Keefe, 2004). Observations from field work also indicate that a notion of "imputed income" was used in a number of provinces. This was a notional level of income that reflected the potential income given the household labor force; this was apparently done with the aim of reducing work disincentives.10 The program also appears to be targeted on the basis of other variables besides income, such as disability. This too could reduce the marginal tax rate facing participants. Since we do not have panel data we cannot observe what happens when benefits are given or withdrawn. The best we can do is use the cross-sectional variance to identify the marginal tax rate. We can estimate the benefit withdrawal rate (BWR) by regressing the per capita DB payment received on income per person less DB receipts, with a complete set of dummy variables for municipalities (to capture the differences in the generosity of the program). The implied BWR is very low, at -0.0012 (t-ratio=-17.51, n=76,808). The estimate is also low if one allows for censoring; using a tobit regression, the estimate was -0.004 (t=-76.23). 10 This is based on a personal communication with Philip O'Keefe. 11 Estimating the tobits separately for each municipality, we obtained statistically significant BWRs in all cases, but all were very low, with none higher (in absolute value) than -0.001. However, there must be a presumption of bias in these estimates, due to measurement error in incomes. There is the usual source of measurement error in asking incomes using only one question, plus the fact that income net of DB payments will probably underestimate income in the absence of DB if there are behavioral responses. To address this concern, we use an Instrumental Variables Estimator (IVE), in which the same set of regressors used in modeling DB participation in the last section are used as instrumental variables (IV) to estimate the BWR. (Note that in this case we only want to know the unconditional regression coefficient of DB payments on pre-DB income, so the instrumental variables are automatically excluded from the main regression of interest. However, the conditional BWR is unidentified.) When we do this, the estimated BWR is -0.0021 (t=-28.33). We also repeated these calculations separately for each municipality, using the IVE for the full sample in each municipality. The estimates were significantly negative for all municipalities and ranged from -0.0102 to -0.0001. These calculations suggest that the marginal tax rate is very small, even allowing for measurement error in incomes. It thus appears unlikely that the program would provide any serious disincentive for earning income. However, at the same time, such a low benefit withdrawal rate raises concerns about how well the program reaches the poorest and how well it adapts to changes in household needs. These observations reinforce the aforementioned concern about how well the program is addressing transient poverty. 4.2 Mean impacts on net income relative to a matched comparison group Another test for behavioral responses is by comparing net income for the DB sub-sample with a matched comparison group. There would (of course) be a strong presumption of selection 12 bias if we were to use non-participants as the comparators. To address this concern we use propensity score matching to select the comparison group from the set of non-participants.11 Predicted values (the propensity scores) from the probit are used for matching.12 Using a light survey instrument will no doubt leave biases in these estimators.13 Given that the program is means tested it is tempting to include income as a predictor of participation in matching. The problem in doing so is that we would then be using the outcome variable (income net of DB) as one of the predictors for estimating impact on that same outcome variable! The results are only unbiased if it is assumed that there are no behavioral effects, which is what one is trying to test. It is not clear what one would then conclude from the results. In general, the direction of bias in the impact estimator cannot be determined.14 To avoid this problem we should exclude income from the probit (using the regression in the Appendix), though then we run even higher risk that we have selection bias based on unobserved variables in the matching. When we exclude income from the probit used to estimate the propensity scores we find that the mean income (net of DB) of participants is significantly lower than income of the matched comparison group of non-participants. Income minus DB receipts is 1417 Yuan lower for the DB participants (with a bootstrapped standard error of 270 Yuan using 100 replications) while mean DB receipts are 270 Yuan. It is not believable that receiving an extra 270 Yuan 11 On the theory of propensity score matching see Rosenbaum and Rubin (1983). For an application to a similar problem to the present one see Jalan and Ravallion (2003). 12 We match each treatment household with the five closest propensity scores. We did not need to drop any observation from the treatment group. The STATA program, nnmatch, was used; results were checked against the program Psmatch2. 13 For evidence on this point in the context of estimating behavioral responses to a cash transfer program in Argentina see Ravallion et al. (2005). 14 We will have underestimated the income net of DB for participants given that they attenuated their labor supply (or received less transfer income) but through the miss-matching we will probably have also underestimated the income of the comparison group (since we over-estimate the propensity scores for treatment units). 13 would result in a reduction in pre-transfer income of 1417 Yuan; indeed, it would not seem plausible that the income loss exceeded 270 on average. This suggests that sizeable selection bias remains in matched comparisons that do not use income as one of the predictors for DB participation. It is of interest to at least see what happens if we use income minus DB as a predictor for participation and then test whether there is any significant difference in income net of DB between participants and the matched comparison group. If we did find such a difference then it would clearly be inconsistent with our maintained assumption that the gain from the program is simply the transfer received from DB. Performing this test, we found that DB participants had a slightly higher income net of DB than the matched comparison group (using net income as a predictor for participation). However, the difference was small and not significantly different from zero; we obtained a difference in mean income of 33 Yuan per person per year, with a bootstrapped standard error (using 100 replications) of 64 Yuan. So the data are internally consistent with the presumption that the income gain is simply the DB payment, though this is clearly a weak test given that the matching is only strictly valid under the assumption that there is no impact on net income. We think it unlikely that single-difference matching is able to deal well with the selection bias in this case. It remains unclear that there is any defensible identification strategy for estimating impacts on net income with these data. However, these observations from the cross- sectional data do not reveal any compelling signs of behavioral responses that would lead one to question whether the income gain is less than the transfer payment. 14 5. Targeting and impacts on poverty We first examine the targeting performance of the DB program, using various measures found in the literature. We then turn to the impacts on poverty. Finally, we examine robustness to measurement errors. Following the results of the last section, we assume that income in the absence of DB is given by the survey-based total income less the amount received from the program. However, we consider alternative welfare indicators that may be less vulnerable to measurement error than our survey-based measures of incomes. 5.1 Performance in reaching the poor Various measures of "targeting performance" are found in the literature, though rarely is much critical attention paid to the properties of these measures. . The first measure we consider would appear to be the most popular one in both the literature and policy discussions. The measure is the share of total DB payments going to those with pre-transfer income Y60 Age of head < 20 0.5902 1.56 0.8190 2.71 20-30 -0.2952 -2.29 -0.3476 -2.89 30-40 -0.0936 -1.53 -0.0757 -1.3 40-50 0.0261 0.48 0.0642 1.23 50-60 0.0499 1.04 0.0806 1.75 Health: Default: head is healthy Disabled 0.8504 16.41 0.9112 18.4 Sick 0.3232 8.88 0.3589 10.24 Years of schooling of head -0.0149 -3.37 -0.0269 -6.64 Head's type of employer: Default: government Public service -0.0696 -0.57 -0.2258 -2.16 State-owned enterprises -0.1827 -1.73 -0.3603 -4.05 Collective enterprises 0.2205 1.89 0.1070 1.04 Share holding enterprises -0.0161 -0.13 -0.1659 -1.51 Private enterprises 0.1894 1.7 0.0564 0.6 Foreign or joined enterprises 0.2382 1.18 -0.0362 -0.19 Self-employed 0.0466 0.43 -0.0991 -1.05 Others 0.3766 3.39 0.2959 3.1 Sector of head. Default: agriculture. Mining 0.3114 1.65 0.1342 0.74 Manufacturing 0.0837 0.86 -0.0557 -0.69 Construction 0.1882 1.62 0.0447 0.43 Transportation 0.0516 0.48 -0.1588 -1.71 Information 0.2442 1.02 -0.0404 -0.19 Retail and whole sale 0.1187 1.16 0.0050 0.06 Tertiary 0.2675 2.16 0.1332 1.21 Banking 0.5134 1.93 0.1884 0.78 Insurance 0.3779 1.05 0.1282 0.4 Real estate 0.2364 1.13 -0.0008 0 Law 0.0882 0.17 -0.2682 -0.58 Accounting -0.1159 -0.47 -0.2995 -1.24 Leasing and commercial service 0.1501 0.76 -0.0133 -0.07 Technological research 0.3087 1.36 0.0587 0.28 Environment 0.0119 0.06 -0.2148 -1.14 Services- agencies 0.4576 2.92 0.3165 2.21 Tourism 0.2107 0.6 0.1362 0.44 Service-others 0.2964 3.1 0.1708 2.15 Education 0.1271 0.63 -0.1503 -0.79 Health 0.2077 1.23 -0.0053 -0.03 Social security and welfare 0.6911 2.98 0.5427 2.56 Publication -0.0083 -0.02 -0.2364 -0.57 Entertainment 0.0859 0.25 0.0515 0.16 39 Culture, sports etc. 0.4005 1.8 0.1680 0.82 Public management 0.2454 2.3 -0.0084 -0.09 Occupation of head. Default: manager Senior professionals -0.1010 -0.36 -0.3269 -1.3 Junior and middle level professionals -0.3455 -2.03 -0.4066 -2.65 General managerial staff -0.1736 -1.72 -0.1533 -1.94 Worker 0.0123 0.14 0.1219 1.73 Others -0.0355 -0.36 0.0953 1.18 Default: head is working Retired 0.3082 3.95 0.1760 2.34 Homeworker 0.4121 4.38 0.2587 2.91 Laid off26 0.3314 4.71 0.2208 3.28 Early retired 0.0009 0.01 -0.2907 -3.26 Unemployed 0.3843 5.38 0.3291 4.82 Student 0.5666 1.53 0.3105 0.91 Other 0.3881 5.57 0.4922 7.6 Assets: Default: Financial assets<10000 Financial assets 10000-30000 -0.4156 -8.17 -0.5592 -11.62 Financial assets 30000-50000 -0.4542 -4.46 -0.6583 -7.25 Financial assets 50000-100000 -0.2933 -2.3 -0.5603 -4.76 Default income less than needed Just right -0.2911 -9.56 -0.4704 -16.78 Surplus -0.4041 -5.44 -0.7047 -10.92 Default income has improved No change -0.2563 -6.82 -0.1669 -4.72 Worse -0.4071 -9.89 -0.2619 -6.79 Wage ratio -0.5899 -16.12 -0.6692 -18.9 Share of retired in h'hold -1.2260 -11.07 -1.5904 -14.8 Share of homeworker -0.2957 -2.56 0.2302 2.16 Share of unemployed 0.2130 2.79 0.5641 7.86 Share of student 0.5245 6.14 0.7343 8.83 Share of children -0.1558 -1.71 0.1202 1.35 City dummy. Default:Beijing Tianjin -0.0681 -0.97 0.0835 1.23 Shijiazhuang -0.2388 -2.78 0.1582 2 Taiyuan -0.5976 -5.42 -0.1291 -1.28 Huhehaote -1.3597 -11.08 -0.9894 -8.55 Shenyang -0.5294 -7.89 -0.1236 -1.94 Dalian -0.5717 -7.65 -0.2926 -4.12 Chuangchun -0.3419 -3.74 0.0560 0.67 Harbin -0.5388 -7.81 -0.0884 -1.39 26 Laid off from SOE with Xia Gang subsidies. 40 Shanghai 0.7573 8.8 0.6718 7.95 Nanjing -0.1851 -2.18 -0.0224 -0.28 Hangzhou -0.3990 -2.72 -0.3229 -2.34 Ningbo 0.0490 0.36 0.1137 0.86 Hefei 0.1415 1.34 0.4473 4.37 Fuzhou -0.5173 -3.8 -0.3696 -2.83 Xiamen -0.3417 -2.32 -0.3485 -2.53 Nanchang -0.2752 -2.77 0.1444 1.57 Jinan -0.4849 -6.06 -0.1259 -1.67 Qingdao -0.7061 -5.58 -0.4098 -3.45 Zhengzhou -0.7907 -6.65 -0.4027 -3.64 Wuhan -0.0319 -0.42 0.3230 4.42 Changsha 0.0645 0.84 0.2039 2.8 Guangzhou -0.6260 -5.01 -0.5750 -4.96 Shenzhen 0.3040 0.97 0.1588 0.64 Nanning -0.5367 -4.17 -0.0279 -0.24 Haikou -1.1193 -7.41 -0.6251 -4.67 Chongqing 0.0532 0.7 0.5052 7.05 Chengdu -0.6369 -3.95 -0.2739 -1.87 Guiyang -0.6384 -6.52 -0.2210 -2.45 Kunming 1.0858 10.24 1.2130 12.44 Xian -0.3491 -2.64 -0.0884 -0.69 Lanzhou -0.4723 -5.36 -0.0964 -1.19 Xining -0.5285 -4.84 -0.2250 -2.27 Yinchuan -0.1434 -1.55 0.2284 2.75 Wulumuqi -1.0720 -8.75 -0.6375 -5.96 Constant 0.3995 0.22 -4.2944 -2.29 # of obs. 76443 76489 Pseudo Rē 0.4718 0.4187 41 Table A3: Summary statistics and measures of targeting and coverage by city (1) (2) (3) (4) (4) (5) (6) (7) DB CR: Mean payment % of SHARE: TD: income DB line per those % of DB Difference in (Yuan (Yuan DB recipient with Y