Abstract
Individuals reject economic inequality if they believe it to result from unequal opportunities. This paper argues income gaps between groups determined at birth, based on sex, race, or family background, can serve people as an indication of unequal opportunities. Findings from a survey experiment show Americans underestimate these gaps. When confronted with accurate information, participants correct their perceptions and adjust redistributive preferences. A follow-up survey finds these effects to last for over one year. In sum, this paper contributes to political economy scholarship that links individual preferences to objective characteristics of the income distribution. Focusing on income gaps offers new ways to explore the political consequences of structural economic change.
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Notes
It is common to focus on birth circumstances as they are clearly beyond individual control.
See https://obamawhitehouse.archives.gov/issues/equal-pay, accessed on September 1, 2017.
Note that surveys most commonly elicit gender, not sex, which is why I refer to the respective gap as gender income gap.
Future studies might want to use more precise signals by accounting for factors such as education, occupation, or working hours. However, a less precise signal was chosen here in order to keep the presentation of the informational treatment as simple as possible.
The size of the income gaps has been calculated for the year 2010, which constitutes the reference year of the project this study was part of (1 citation removed for masked review), based on data from the Panel Study of Income Dynamics. In order to reflect labor market differences and not the redistributive effects of taxation, before-tax income data were used. These data include income from both employment and self-employment, but not income from property or other investments. All incomes were adjusted for life-cycle variations by correcting for systematic differences based on a cubic regression of income on age to account for potential compositional differences across groups. As it is common in the USA to indicate income in annual values, the same time reference is used here.
This is the percentage of those who provided their e-mail in the first survey. A small amount of messages was returned due to incorrect or expired addresses.
Different from its use here, some social justice research uses this item to measure the latent concept of “egalitarian ideology”.
Results regarding the proposed hypotheses are not driven by this specification. Table 14 in Appendix 1 shows that they hold if redistribution preferences are treated as a continuous variables (although in one specification only for a low level of statistical significance).
Alternative link function which is often used for dichotomous dependent variables, such as logit or probit, would due to their nonlinearity necessitate different assumptions about how individuals incorporate new information, i.e., not Bayesian updating. That being said, the results are robust to using these alternative link functions.
Gender income gap, t = 26.779, p = 1.000; race income gap, t = 26.826, p = 1.000; intergenerational income gap, t = 32.641, p = 1.000).
All models control for a round dummy indicating whether the respondent was recruited in May or July round of 2016.
Table 2 shows that the design-only model (1) explains about 3.5% of the variation in the dependent variable (see R\(^2\)). Removing the treatment indicator and its interaction with Prior(Gaps) reduces the explained variance to 0.7% (see Table 5, Model 1). This implies that new information is not only statistically significant but also substantively important. For further comparisons between the results presented in the main text and baseline models the reader can refer to Table 5.
One might be concerned that this reversal in the effect might is driven by extrapolation. I address this issue in Appendix 3 by separately estimating treatment effect for each Prior(Gaps) decile. It turns out that the decile with the highest perceptions indeed responds negatively to treatment (although not at statistically significant levels); thus, the reversal is not driven by extrapolation.
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Acknowledgments
Bastian Becker has received a research grant from the Central European University (Grant No. 2014/2015/1/RSS)
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Appendices
Appendix 1
See Tables 3, 4, 5, 6, 7, 8, 9, 10, 11, 12, 13, 14, 15 and 16.
Appendix 2
Average treatment effect on agreement with redistribution conditional on prior perceptions of income gaps, by gender (initial survey). Note: Conditional average treatment effects (vertical axis) as change in predicted probability (percentage points) of agreeing with redistribution, based on separate models 1-8 (Table 6). Prior(Gaps) refers to the mean prior income gap perception. Confidence intervals (90%) based on bootstrapped model parameters (N=100,000). Gray shading indicates distribution of prior perceptions (kernel density estimation, bandwidth=500)
Average treatment effect on agreement with redistribution conditional on prior perceptions of income gaps, by race (initial survey). Note: Conditional average treatment effects (vertical axis) as change in predicted probability (percentage points) of agreeing with redistribution, based on separate models 1–8 (Table 8). Prior(Gaps) refers to the mean prior income gap perception. Confidence intervals (90%) based on bootstrapped model parameters (N=100,000). Gray shading indicates distribution of prior perceptions (kernel density estimation, bandwidth=500)
Average treatment effect on agreement with redistribution conditional on prior perceptions of income gaps, by parental education (initial survey). Note: Conditional average treatment effects (vertical axis) as change in predicted probability (percentage points) of agreeing with redistribution, based on separate models 1–8 (Table 10). Prior(Gaps) refers to the mean prior income gap perception. Confidence intervals (90%) based on bootstrapped model parameters (\(N=100,000\)). Gray shading indicates distribution of prior perceptions (kernel density estimation, bandwidth = 500)
Appendix 3
Linearity of Treatment Effects
Above analysis posited a linear relationship between prior perceptions and the strength of the treatment effect. Other specifications would require stronger assumptions about how individuals process information. To determine whether positing a linear relationship is warranted I estimate separate regression models for each decile of the Prior(Gaps) distribution. Figure 9 displays the treatment effects estimated for each decile. Confidence intervals are wide as the number of observations for each regression is only one-tenth of the total sample. The figure attests to clear deviations from a perfectly linear, or even monotonous, relationship. In particular, the treatment effect falls off among those in the lowest decile, whose average prior perception is below US$4000. One explanation might be that respondents with such low income gap perceptions might find information on the actual extent of income gaps hard to believe. Another deviation from a linear relationship is the steep decline in the treatment effect between the fourth and fifth decile. The difference between the two deciles accounts for much of the decline observed over all deciles (Fig. 9).
LPM results, effects on agreement with redistribution, by average prior perception deciles (initial survey). Note: Local average treatment effects (vertical axis) as change in predicted probability (percentage points) of agreeing with redistribution. Horizontal axis indicates Prior(Gap) decile based on which OLS regression models were estimated. Models include treatment status and round dummy. Confidence intervals (90%) based on bootstrapped model parameters (\(N=100,000\))
Another important aspect of Fig. 9 is that the treatment effect for the tenth decile strongly points into a negative direction. These respondents become more likely to disagree with redistribution when confronted with factual information. This is in fact what would be expected. With average prior perceptions of US$20,000 or higher, these respondents overestimated the actual size of the gaps. Therefore, confronting them with factual information should reduce their concern about income gaps and hence demand for redistribution. This corroborates the findings presented in Fig. 3 and affirms that the changing sign of the treatment effect is not driven by extrapolation. Overall, the separate regressions attest to a decline in the treatment effect that is sufficiently steady to assume a linear relationship between prior perceptions and the effect of factual information.
Appendix 4
Attrition Analysis and Inverse Probability Weighting
Experiments that stretch longer time periods unavoidably face attrition, which can lead to bias in the estimation of treatment effects. The high response rate to the second survey is not sufficient to exclude the possibility of such a bias. Therefore, it is important to check for indications of attrition bias. This is done similarly to how researchers check for covariate balance in single-shot experiments. Just as in the case of covariate balance, it is only possible to check for attrition bias based on observables. While the absence of such a bias for observables can increase our confidence in the unbiasedness of results, it is no guarantee (Tables 17, 18).
The most basic source of attrition bias is differential response rates across experimental conditions. Furthermore, it would be worrisome if attrition patterns based on covariates differed between control and treatment group. In order to assess these sources of bias, I run separate regressions for both experimental groups. I begin with an intercept-only model and continue with univariate regressions for the main socio-demographic covariates elicited in the initial survey. Results are shown in Table 17. The response rates of both groups are not exactly the same, 40.7% for the control group and 38.7% for the treatment group. However, as the right-most columns show, the difference is not statistically significant.
There is some evidence, especially in the control group, that respondents who are male, retired, and/or older are more likely to drop out. However, in no case is this pattern significantly different between both groups. There is also no evidence that respondents who took more time for the first survey are more likely to drop out. Finally, it is possible to check for attrition based on the two central variables in this study, respondents’ prior perceptions of income gaps and preferences for redistribution. As these variables are constitutive of the causal mechanism explored here, attrition bias would be detrimental. Fortunately, there is no indication of any bias with regard to either variable.
As discussed above (see The Income Gaps Experiment), one approach to address imbalances due to attrition is inverse probability weighting. These weights are based on each respondent’s probability to participate in the follow-up survey. Table 18 presents the model based on which these probabilities are estimated.
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Becker, B. Mind the Income Gaps? Experimental Evidence of Information’s Lasting Effect on Redistributive Preferences. Soc Just Res 33, 137–194 (2020). https://doi.org/10.1007/s11211-019-00343-7
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DOI: https://doi.org/10.1007/s11211-019-00343-7