Welfare programs are important in terms of reducing poverty, although they create incentives for recipients to maximize their income by either reducing their labor supply or manipulating their taxable income. In this paper, we quantify the extent of such behavioral responses for the earned income tax credit (EITC) in the USA. We exploit the fact that US states can set top-up rates, which means that at a given point in time, workers with the same income receive different tax refunds in different states. Using event studies as well as a border pair design, we document that raising the state EITC leads to more bunching of self-employed tax filers at the first kink point of the tax schedule. While we document a strong relationship up until 2007, we find no effect during the Great Recession. These findings point to important behavioral responses to the largest welfare program in the USA.
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A key result of the existing literature on labor supply reactions to the EITC is that there are positive effects at the extensive margin (Eissa and Liebman 1996; Meyer and Rosenbaum 2001; Grogger 2003; Hotz and Scholz 2006; Gelber and Mitchell 2012). This result, which was found primarily for single mothers, does not hold true for secondary wage earners, for whom Eissa and Hoynes (2004) find a decrease in participation. In contrast to these findings, previous research suggests that there are none or only small effects at the intensive margin (Rothstein 2010; Chetty and Saez 2013).
See Fig. 6 in Appendix A for an illustration. For families with two children, the kink points for 2009 are at $12,570 and $16,420. The maximum tax credit is $5,028, which results in steeper phase-in and phaseout regions compared to the schedule for families with one child.
Wisconsin has a top-up rate of zero for childless people, but top-up rates of 4, 14 and 43% for families with one, two and three and more children, respectively.
We are aware that DC is technically not a state. However, it has its own EITC.
To put these numbers into perspective, in 2009, the total number of people with income from self-employment was 16.8 million, which represents 10.7% of the workforce (Source: Social Security Administration). According to Chetty et al. (2013), the share of self-employed EITC claimants was 19.6%, whereas the share of EITC-eligible filers among all tax filers was 18.9% (Source: Brookings Institution, Characteristics of EITC-eligible tax units 2015). Therefore, the share of filers that were both eligible for the EITC and had income from self-employment was around 3.7%.
For this reason, our analysis spans these years, although in the future it would be desirable to have data past 2010, which would allow us to study the effects of the EITC during and after the Great Recession. In Appendix D, we explain in greater detail how we convert zip-code-level information to the county level.
As explained in footnote 14 in Chetty et al. (2013), the results are robust to (i) defining the denominator of the bunching measure using only self-employed individuals rather than the full population, (ii) the choice of bandwidth around the kink point and (iii) a measure whereby bunching is measured as the excess mass over a smoothly fitted polynomial within a certain bandwidth.
See Feenberg and Coutts (1993) for a documentation.
In our main analysis in Sect. 5, these county pairs will be included. We also performed the event study including these cases. The results remain unchanged. The tables are available from the authors upon request.
While these two dummies are multicollinear, it is possible to include these interactions in the regression because we do not include the dummies on their own.
Sources: minimum wages: St. Louis Fed, welfare benefits: welfare rules databook, tax revenue: Annual Survey of State Government Tax Collections, consumer price index: St. Louis Fed, marginal income tax rates: NBER TAXSIM.
We found splitting the number of claimants evenly between counties the most transparent way of converting zip-code-level data to county-level data. It would also be possible to (dis-)aggregate the numbers based on population measures. However, without further assumptions, this would only be possible for disaggregation (one zip code contains more than one county), but not for aggregation (one county contains more than one zip code).
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We would like to thank the editor, two anonymous referees, David Agrawal, Jacob Bastian, Manasi Deshpande, as well as audiences at IZA, ZEW, the IIPF 2017 in Tokyo, and the NTA 2017 in Philadelphia for their helpful comments.
Appendix A: The EITC tax schedule
Figure 6 illustrates the EITC tax refund schedule for families with one and two children. The refunds refer to 2009, the last year in our sample.
Appendix B: Predicting EITC expansions
Our identification strategy relies on the assumption that the top-up rate in a state is uncorrelated with county or state characteristics. A central concern with this assumption is that the generosity of the state EITC is driven by the business cycle, state-level fluctuations in tax revenue, or changes in minimum wages. To address this concern, we follow Bastian and Michelmore (2018), and predict the level of the state EITC based on current and lagged state-level economic variables in a panel regression. If any of the variables turned out to be statistically significant, this would be reason for concern, as it would cast doubt on the validity of the identifying assumption.
For this purpose, we collected state-level data on the welfare state (top marginal income tax rate, level of minimum wage, monthly welfare benefits), as well as tax revenues, which can be seen as a measure of the business cycle. The data span the years 1995–2009.Footnote 16 The regression results are shown in Table 4. Given that statistically insignificant results are more likely when standard errors are clustered, we report here conventional standard errors. None of the regressors is statistically significantly different from zero, which we interpret as strong evidence that changes in the state EITC are not driven by state-level fluctuations in the economy.
Appendix C: EITC claimants before, during and after the Great Recession
Figure 7 displays the number of EITC claimants around the time of the Great Recession, between 2007 and 2012. This number has been increasing throughout, although the increase was strongest during the Great Recession, between 2008 and 2009.
Appendix D: Converting zip-code-level data to county-level data
The dataset by Chetty et al. (2013) provides data at the level of three-digit zip codes. Because the border pair design requires information at the county level, we convert the data from the zip code to the county level. The dataset mainly consists of absolute numbers, such as the number of EITC claimants in a given zip code. If a zip code comprises more than one county, we divide the absolute numbers evenly across all counties within a zip code. For example, if there are 1000 claimants in zip code A and A consists of two counties, we assign each county 500 claimants. If, on the other hand, a county is part of more than one zip code, we assign this county the sum of the absolute numbers. If the zip code that cuts through a county also covers another county, we split the absolute numbers between these countries before adding up within counties. For example, if zip codes A (1000 claimants) and B (500 claimants) are completely contained in county X, we assign county X 1500 claimants. If, however, zip code A also covers another county while B is fully contained in X, we assign county X 500 claimants from A and 500 claimants from B.Footnote 17
For the 3141 counties in our dataset, we apply the first method—split the numbers between counties within a zip code—to 1179 counties. For another 1960 counties, we apply both methods, namely we split numbers between counties as well as aggregate numbers within counties. The remaining two counties coincide with the zip codes.
Appendix E: Identifying variation
Table 5 displays the amount of variation—measured by the standard deviation—in the most important variables for different samples as well as different fixed effect specifications. Column (1) displays the variation for all counties, whereas Columns (2)–(4) display the variation for border counties only. In the border pair sample, some counties appear more than once if they have more than one neighbor in a different state. Going from left to right, one can see that the amount of variation is reduced as more fixed effects are added. However, even after controlling for pair-by-year fixed effects, there remains substantial variation in top-up rates as well as the outcome variables.
Figure 8 further illustrates the relationship between state-specific top-up rate (horizontal axis) and the degree of bunching (vertical axis) in a binned scatter with ten equally sized bins on each axis. The graph controls for state-specific characteristics of the EITC—a dummy that equals unity if the refund depends on the number of children, and a dummy that equals unity if a positive refund is given if a person’s tax credit exceeds his/her tax liability—as well as pair-by-year fixed effects. The regression line corresponds to the regression coefficient in Table 2, Panel A), Column (4).
Appendix F: Assessing inference through permutation tests
While the border design facilitates estimating a causal effect by providing clear treatment and control counties, it also complicates statistical inference. The error terms can be correlated across space as well as within counties over time, which can lead to an underestimation of standard errors, and an under-rejection of the null hypothesis of no effect (Bertrand et al. 2010). Moreover, in the border pair design, some counties are part of multiple pairs, such that their errors are mechanically correlated. As a first step, to account for correlations in the error term, we applied to all estimates a two-way clustering procedure at the county and pair level. However, this may not eliminate all systematic correlations of the error terms.
To assess the statistical significance of our estimates without relying on assumptions about clustering, we additionally perform permutation tests for the four main outcomes. In these tests, we first obtain an empirical placebo distribution of estimates that would occur under the null hypothesis of there being no effect. In a second step, we compare our estimates to the placebo distribution and obtain an empirical p value that describes the probability of obtaining a result that is at least as extreme as ours.Footnote 18 In a conventional case—namely one in which a treatment is assigned once—the placebo distribution is obtained by repeatedly randomizing the treatment across observations and estimating the same model in each replication. The complication in our case is that top-up rates within states are path-dependent. States do not randomly set a top-up rate every year, but rather adjust the rate of the previous year. To account for path dependency, we therefore randomize over 14-year paths in top-up rates. In each replication, we randomly assign each state a path for its top-up rate and estimate the model.
Figure 9 displays the cumulative density function of the placebo distributions based on 5000 replications, as well as the z-scores of our estimates (vertical lines) from Column (6) in Table 2. The horizontal lines describe the 90-th percentile of the placebo distribution. Statistical significance at the 10% level requires that the intersection of both lines is located southeast of the placebo distribution. This is the case for the outcomes displayed in Panels A-C, where the empirical p values are 0.055, 0.014, and 0.027, respectively. For the outcome in Panel D—namely the total number of non-self-employed claimants—the p value is 0.128, which means that this estimate is not statistically significant at the 10% level.
These results confirm the inference drawn from the two-way clustering approach in Table 2. Raises in the top-up rate significantly increase bunching near the kink point, which is the result of an overproportional increase in the number of claimants with an income close to the kink point. As before, we find no statistically significant effect on the total number of non-self-employed EITC claimants.
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Buhlmann, F., Elsner, B. & Peichl, A. Tax refunds and income manipulation: evidence from the EITC. Int Tax Public Finance 25, 1490–1518 (2018). https://doi.org/10.1007/s10797-018-9510-7
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