After winning the 2024 U.S. presidential election, Donald Trump instituted a series of high-profile reforms, firing thousands of federal workers and instituting tariffs on almost every country. Alongside these events, survey measures of partisan differences in economic perceptions shifted dramatically. In November, the University of Michigan’s Survey of Consumers found that Democrats viewed the current economy more favorably than Republicans by a 91-38 margin on the Index of Consumer Sentiment. By April, Republicans were more favorable by an 81-53 margin. The 2024–2025 flip was unusual in its magnitude, with both Democrats and Republicans shifting by more than either party had shifted in any of the past three election cycles (Figure 1). Observers often point to these post-election partisan flips as evidence of partisan expressive responding, wherein Democrats and Republicans offer survey responses that are more partisan than their underlying beliefs (Bullock et al., Reference Bullock, Gerber, Hill and Huber2015; Prior et al., Reference Prior, Sood and Khanna2015; Edwards-Levy, Reference Edwards-Levy2022; Burn-Murdoch, Reference Burn-Murdoch2023). On the other hand, Malka and Adelman (Reference Malka and Adelman2023) argue that evidence of expressive responding is limited when it comes to politically salient topics.
Post-election flips in economic perceptions, 2008–2009 to 2024–2025.
Note: Figure displays the index of current economic conditions from the University of Michigan Survey of Consumers. See “Table 5B. The Index of Consumer Sentiment with Current and Expected Components within Political Party,” accessed July 15, 2025.
To test for expressive responding in this context, I fielded a survey experiment using Prolific in April–May 2025 (
$N$
= 2,831). Shortly before the releases of official estimates of three objective economic indicators — GDP growth, inflation, and unemployment — respondents were asked to guess what the value of the current month or quarter’s statistic would turn out to be. Randomly selected respondents were offered a $2 incentive to guess correctly. The expectation is that if expressive responding is present, payment would reduce partisan differences in guesses. The design also featured four mechanism checks designed to distinguish between two competing explanations for the effect of pay-for-correct treatments (Prior et al., Reference Prior, Sood and Khanna2015; Bullock & Lenz, Reference Bullock and Lenz2019). The misreporting explanation holds that payment makes partisans less likely to intentionally misreport their beliefs, while the congenial inference explanation holds that payment encourages more even-handed reasoning.
Little evidence of expressive responding emerged. Relative to the average Democrat, the average Republican guessed the economy was be 0.44 standard deviations better in the control group versus 0.38 standard deviations better in the treatment group, a statistically insignificant difference of about 0.06 standard deviations. An alternate coding based on the predicted direction of change yielded even less evidence of expressive responding, with a point estimate of almost exactly zero. The lack of movement on the primary dependent variable limits what can be learned from the mechanism checks. However, two measures of response effort (response time and looking up information) increase substantially. This suggests that there is more to pay-for-correct treatments than reducing misreporting but does not say enough about the nature of the increased effort to confirm the congenial inference explanation.
Approach
To test for expressive responding in the wake of Trump’s return to office, I adapted variant of pay-for-correct experiments (Bullock et al., Reference Bullock, Gerber, Hill and Huber2015; Prior et al., Reference Prior, Sood and Khanna2015). In pay-to-predict experiments, randomly selected respondents are offered financial incentives to predict the outcome of objectively verifiable events that have not yet occurred. The fact that the true outcome is not yet known forces respondents to apply their general domain-relevant beliefs to the specific fact they have been asked to predict and at the same time removes the threat that the incentive will induce respondents to look up the correct answer. Two recent articles use this strategy. Studying perceptions of the COVID-19 pandemic, Allcott et al. (Reference Allcott, Boxell, Conway, Gentzkow, Thaler and Yang2020) offer financial incentives for accurate predictions of the number of cases at a future date. This encourages people to apply their general beliefs about the severity of the pandemic to a specific number that cannot yet be looked up. Studying beliefs about Donald Trump’s claim that the 2020 election was stolen, Graham and Yair (Reference Graham and Yair2024) ask respondents to predict whether a conspiracy theory involving the emergence of evidence for those claims would come to fruition. This encourages people to apply their beliefs about the veracity of the theory to a concrete event that will only come to pass if the theory is true.
To capture general economic perceptions in a way that is compatible with payment for correct answers, I take advantage of the regularly scheduled release of official economic statistics. Just prior to the release of official statistics, all of the policy changes, news events, and personal experiences that affect economic perceptions have already occurred even though objective measures of those conditions are not available. This forces one who is trying to guess the statistic’s value to rely on more general considerations. Even when the truth is known, existing research interprets numerical questions about statistics in this manner. Kuklinski et al. (Reference Kuklinski, Quirk, Jerit, Schwieder and Rich2000) argue that although people do not form beliefs about “details such as specific amounts and percentages in the ordinary course of events … When they have the occasion — for example, answering a survey — they will translate these general notions into more specific ones” (795). Ansolabehere et al. (Reference Ansolabehere, Meredith and Snowberg2013) show that providing benchmark values helps respondents apply their generalized economic perceptions to more specific questions about economic statistics.
Existing research furnishes two accounts of how randomly assigned payments affect survey responses. Bullock et al. (Reference Bullock, Gerber, Hill and Huber2015) propose that financial incentives reduce insincere misreporting, which they term “partisan cheerleading.” According to this account, respondents form the same belief in both conditions but choose to report a different, more partisan-friendly belief when financial incentives are absent. Another account, congenial inference, holds that financial incentives affect how people reason and, consequently, their on-the-spot judgments about survey questions (Prior et al., Reference Prior, Sood and Khanna2015; Khanna & Sood Reference Khanna and Sood2018; Bullock & Lenz, Reference Bullock and Lenz2019). According to this explanation, financial incentives heighten accuracy motivations at the expense of directional motivations, encouraging respondents to canvass the information they hold in memory more even-handedly and to weigh it more objectively when aggregating it into a summary judgment about the survey question. This results in responses that are equally sincere — but, owing to the more objective process of converting considerations into survey responses, are more reflective of respondents’ underlying perceptions. There is little basis in existing research to adjudicate between these accounts (Bullock & Lenz, Reference Bullock and Lenz2019). Graham (Reference Graham2025a ) suggests that supplemental outcome measures may help distinguish between them.
Research design
To implement this approach, I fielded a panel survey through Prolific in 2025. On April 21, Wave 1 collected background characteristics and pretreatment measures of all outcome measures (N = 3,769). After a series of quality filters, including a captcha, bot detection, indicators of frequent window-switching, and attention to instructions, 3,046 respondents were invited to participate in the experiment. The experiment was conducted in two subsequent surveys just before the scheduled release of economic indicators. Wave 2 (April 26–29, N = 2,693) covered quarterly GDP and April unempoyment, which were released on April 30 and May 2. Wave 3 (May 7–12, N = 2,579) covered April inflation, which was released on May 13. In each wave, respondents were independently randomly assigned to one of the two treatment conditions; assignments were allowed to differ between Wave 2 and Wave 3. More information about the samples, preregistration (aspredicted.org/fqtw-hytf.pdf), and survey instruments appears in Appendix A.
In the experimental waves, the questions about each economic indicator followed the same sequence. First came an open-ended questions designed to measure the content of respondents’ reasoning. For example, the open-ended unemployment question read,
On the next page, we’ll ask you to guess the official unemployment rate for the month of April. It will be published on Friday. The March rate was 4.2%.
IF TREATED: If you guess the April unemployment rate correctly, we will pay you a $2 bonus on Friday morning.
First, we’d like you to think about it. Please write down what thoughts come to mind as you try to guess the April unemployment rate. (We want to know what you’re thinking about, not the number. You’ll make your guess on the next page.
If the congenial inference explanation is true, treated respondents should reason more even-handedly in anticipation of the bonus, reporting less partisan considerations. In contrast, since the financial incentive is tied only to an accurate guess of the unemployment rate, there is no incentive to misreport one’s open-ended thoughts. Two scoring rules were used to summarize the open-ended questions: positive and negative sentiment (Pröllochs et al., Reference Pröllochs, Feuerriegel and Neumann2018) and the “implied words” method, which classifies short text based on how often each word appears with each other word across the entire corpus (Hobbs & Green, Reference Hobbs and Green2025). For example, if the words jobs and unemployment tend to appear together, the method is designed to recognize that a response that includes the word jobs but not the word unemployment is still probably “about” unemployment.
Following the open-ended question, respondents were asked for their numerical guess. The unemployment question read,
On Friday, the Bureau of Labor Statistics will release the official unemployment rate for April. The March rate was 4.2%.
What do you think is the April unemployment rate?
Please enter a number between 0.0% and 10.0%. You can use up to 1 decimal place
IF TREATED: Remember that if your guess is correct, we will pay you a $2 bonus after the rate is published on Friday morning.
Prior to estimating treatment effects, I reverse the inflation and unemployment scales so that larger values are considered good, then transform all measures in two ways. First, the “standard deviations” measure subtracts the control mean and divides by the control standard deviation. This procedure, variously known as standardization or Cohen’s D, expresses differences and effects in terms of the number of standard deviations. Second, the “net direction of change” measure scores each response in terms of whether it implies the indicator will get worse (−1), stay the same (0), or get better (1). This measure is equivalent to subtracting the proportion who say each indicator will get worse from the proportion who say it will get better.
As respondents answered the open-ended questions and primary dependent variables, two supplemental outcome measures designed to capture reasoning effort were simultaneously collected. If the congenial inference account is correct, treatment increases accuracy motivation, which should result in greater response effort. In contrast, if misreporting alone can explain the effects, there should be no change in response effort. Response time was the first measure of effort. The number of seconds spent on the open-ended and numerical questions was added, trimmed at 300, and logged. The second measure of effort, window-switching, tests whether the treatment affects people’s propensity to look up information. Although people can switch windows during a survey for a number of reasons, existing research finds that a large majority of respondents who switch to a different window on their device are looking up information (Graham, Reference Graham2024). The window-switching variable equals 1 if the respondent window-switched on either the open-ended or numerical question and 0 otherwise.
Following the objective questions, respondents were asked two questions about subjective economic perceptions from the American National Election Survey (ANES): a question about current conditions (“What do you think about the state of the economy these days in the United States? Would you say the state of the economy is good or bad?”) followed by a question about expectations (“What about the next 12 months? Do you expect the economy in the country as a whole to get better or worse?”). Both used five-point response scales (Appendix A). If the financial incentive induced respondents to call different information to mind when answering the objective question, this information should still linger in memory on the following questions, effectively functioning as a prime. On the other hand, if the financial incentive merely reduces misreporting, there should be no such effect. In fact, if incentives induce treated respondents systematically pass up misreporting opportunities on objective questions, respondents may have a greater need to “blow off steam” (Yair & Huber, Reference Yair and Huber2020) when they reach the subjective questions, potentially increasing partisan misreporting.
Bonuses were paid soon after the surveys ended. On April 30, one day after Wave 2 ended, the Bureau of Economic Analysis released its preliminary estimate of real GDP growth for the first quarter, −0.3%.Footnote 1 , representing a substantial decline from the prior year’s rate of 2.8%. Of the eight respondents who guessed correctly, two were in the treatment group and received a $2 bonus. Two days later on May 2, the Bureau of Labor Statistics released the April unemployment rate, 4.2%, which was unchanged relative to March.Footnote 2 Of the 221 who guessed correctly, 124 were in the treatment group. On May 13, one day after Wave 3 ended, the Bureau of Labor Statistics released the 12-month inflation rate for April 2024–25, 2.3%. This was 0.1% lower than the March 2024–25 rate.Footnote 3 Of the 183 who guessed correctly, 114 were in the treatment group.
Results
Do objective measures capture general perceptions?
The notion that people answer survey questions about objective economic indicators based on general perceptions, as opposed to preexisting beliefs about the specific number, is supported by some existing research (Kuklinski et al., Reference Kuklinski, Quirk, Jerit, Schwieder and Rich2000; Ansolabehere et al., Reference Ansolabehere, Meredith and Snowberg2013) but has not been tested in the expressive responding literature. Accordingly, Figure 2 displays the wave-to-wave correlations between the subjective and objective measures of economic perceptions for respondents assigned to the no-incentive condition. Rows represent the wave 1 measure while columns represent the nearly identical wave 2 or 3 measure.
Between-wave correlations.
Note: For respondents assigned to the control (no-incentive) condition, figure displays the correlation between the wave 1 and wave 2 or 3 measures of all outcomes that were measured pretreatment. The left panel uses the variables in their natural units. Identical results obtain when the variables are standardized. The right panel uses the sign of each variable.
For the objective measures, the between-wave correlations are modest at best. When GDP growth is measured in its natural units (left panel), the correlation between the wave 1 and 2 responses is 0.49, while the inter-wave correlations between GDP and the subjective measures range from 0.34 to 0.41. When GDP growth is scored in terms of the direction of change, the correlations are even more similar (0.38 versus 0.28 to 0.41). For unemployment, the correlations are somewhat lower. The correlation between the two unemployment measures is only modestly higher than those between unemployment and the subjective measures (0.28 versus −0.15 to −0.27) and falls in the same range with the direction of change scoring (0.36 versus −0.22 to −0.41). The inflation correlations are lower still, with the same pattern of similarity between the objective–objective and subjective–objective correlations (in standard deviations, 0.19 versus −0.15 to −0.22; direction of change, 0.26 versus −0.18 to−0.29). Here, two key patterns emerge: (1) responses to objective measures are not especially stable across survey waves and (2) the between-wave correlations between objective and subjective measures are similar to the correlations between identical objective measures. This suggests that although guesses about the value of objective economic indicators are noisy, general perceptions constitute much of the systematic component.
Respondents appear to have had an easier time connecting subjective questions to their economic perceptions. The between-wave correlations between identical subjective questions range from 0.67 to 0.82. This suggests that relative to objective questions, people have an easier time connecting subjective questions to their underlying beliefs. When one subjective question is used to predict another, the correlations range from 0.56 to 0.64. This is also higher than any objective question’s correlation with any question. In other words, the two subjective questions predict one another better than the objective questions predict themselves.
Among the three objective questions, the GDP growth question appears to tap general economic perceptions most effectively. It is the most stable: the between-wave correlations for guesses about GDP growth (0.49 and 0.38) were higher than the equivalent figure for unemployment (0.28 and 0.36) and inflation (0.19 and 0.26). It also has the highest correlations with the subjective measures. However, two other factors could have contributed to inflation’s poor performance. First, there was more time between the surveys: the wave 2 survey containing GDP and unemployment launched 5 days after the baseline survey, whereas the inflation survey launched 17 days later. Splitting across two survey waves allowed each part of the experiment to be conducted within a week of the release of the relevant economic indicator, hopefully increasing the credibility of the bonus payment and minimizing the role of impatience but also allowing more time for genuine change. Second, the inflation question wording changed between the two survey waves. In an effort to better target the perceived effects of the April tariff announcements, Wave 1 asked about monthly inflation, but the distribution of responses suggested that many respondents were trying to guess annual inflation (Appendix A.4). Accordingly, I changed the experimental question to ask about annual inflation.
Effect on objective measures of perceptions
As a first look at the experimental results, Figure 3 displays the response distributions in the treatment group (solid colored bars) and the control group (hollow bars). On all three questions, responses cluster around the dashed vertical line representing the previous month’s value of the statistic. Relatively to Democrats, more of Republicans’ probability mass lies in the area representing an increase in GDP growth, decrease in inflation, and decrease in unemployment. This is a typical pattern of partisan difference, wherein the party in power is more optimistic about the state of the economy (Bartels, Reference Bartels2002; Figure 1). When the variables are examined in their natural units, the average difference between the parties is substantively large for GDP growth (1.1 pp) and modest for the other two variables (0.2 pp for inflation, 0.3 pp for unemployment; Table 1). These differences seem larger when one considers that most respondents stay within a few tenths of the reference points. In terms of the direction of change, Republicans are about 50 pp more optimistic on all three measures.
Response distribution by treatment group.
Note: Figure displays distributions of responses to objective questions. Hollow bars are the control group. Solid colored bars are the treatment groups. Dashed vertical lines display the rate for the previous month or quarter, which was stated in the wording of the question.
To illustrate how the separate questions are aggregated into statistical tests, Table 1 displays the treatment and control means for each measure, as well as three measures of partisan difference: the difference in their natural (untransformed) units and the two transformations described above, standard deviations and the direction of change. For each question and transformation, there are two estimates of the treatment effect. The first estimate, unadjusted, is the difference between the treatment and control means just above. The second estimate, adjusted, is estimated using regression with controls for pretreatment covariates; the preregistration specifies that the adjusted estimates are preferred. At the bottom of the table, the “pooled” row presents the results of the aggregate test.Footnote 4 Regression tables containing the same estimates appear in the appendix (Tables A2 and A3).
There is not much evidence that the pay-for-correct treatment reduced partisan bias. In the bottom row of Table 1, neither pooled test is statistically significant at the
$p \lt 0.05$
level (one-tailed). The point estimate for the standard deviation measure suggests a small reduction of partisan differences equal to about 13 percent of the baseline,Footnote
5
while the point estimate for the direction of change measure is almost exactly zero. The top three rows display equivalent estimates for each individual question. None of the question-level results is so stark as to fundamentally change the conclusions: one of the six estimates suggests a statistically significant decline in partisan differences, but this only holds for one of the two codings of the outcome measure.
To better contextualize the null result I conduct equivalence tests, which gives the range of null hypotheses that could not be rejected. Rainey (Reference Rainey2014) shows that a 90 percent confidence interval is equivalent to the range of effect sizes that could not be ruled out at the 5 percent level, one-tailed. Figure 4 visualizes the treatment effects and equivalence bounds relative to the control group. The solid bars represent the control means from Table 1, hollow bars, the treatment means; arrows, the direction and magnitude of the treatment effect estimate; and dark gray bands, the equivalence bounds. Using the standardized measure, the equivalence bounds suggest that treatment effects of more than one-third of the baseline are unlikely. Using the direction of change, effects of more than about one-sixth of the baseline in either direction are unlikely. On a question-by-question basis, large effects can be ruled out for all but the inflation question, which again is dependent on the scoring rule.
Equivalence bounds relative to baseline differences.
Note: Figure displays treatment effect estimates on the difference between Republicans and Democrats. Left panel displays effect on standardized variables. Right panel displays effect on direction of change. Hollow bars display partisan difference in the control group. Solid gray bars display treatment mean. Below the bars, dark gray band displays the 90 percent confidence interval for the treatment effect, centered at the treatment group mean; this visualizes the range of plausible effects relative to the control group. The same estimates appear in the summary table above (Table 1) and in the appendix (Tables A2 and A3).
Effect on response effort
There is clear evidence that treatment induced greater response effort. In the control group, the average respondent spent 116 seconds answering the objective questions, including the preceding open-ended question. In the treatment group, the average respondent spent 130 seconds. For a statistical test of the difference, I first trimmed the response times at 300 seconds, which reduces the averages to 106 and 120 seconds. I then took the natural log of the trimmed response time variable, giving the estimates a percent change interpretation. On average, response time in the treatment group was about 14 percent higher than in the control group (s.e. = 1.5; Table 2, column 2).
Mechanism checks: Effort
Note: Table displays treatment effect estimates for measures of response effort. Columns 1 and 3 display difference in means estimates. Columns 2 and 4 display covariate-adjusted estimates based on the preregistered estimation procedure. Appendix Table A4 displays the same table with all control variables.
Treated respondents were also more likely to look up information. For each question, an indicator variable measures whether the respondent was flagged for looking up information on either the open-ended or objective question. Coefficient estimates represent the average of the three questions. In the control group, about 14.3 percent of respondents were flagged for window switching. Treatment increased the proportion looking up the answer by about 6.5 percentage points, about a 45 percent increase relative to the baseline.
Effect on content of reasoning
Conditional on the amount of reasoning that respondents engaged in, there is no evidence that the treatments affected the content of respondents’ reasoning. Table 3 presents the estimated effects on partisan differences positive/negative sentiment, the implied words score, and the subjective measure. None are statistically significant, and all of the point estimates are either very close to zero or correspond to an increase in partisan differences. As a robustness check on the fact that both scorings of the open-ended responses (sentiment and implied words) involve scaling the responses, Appendix B.2 presents an exploratory test based on the change in the average absolute difference in implied word scores, with the same result.
Mechanism checks: Content of reasoning
Note: Table displays treatment effect estimates for measures of the content of reasoning. Columns 1, 3, and 5 display unadjusted estimates. Columns 2, 4, and 6 display covariate-adjusted estimates based on the preregistered estimation procedure. Appendix Table 8 displays the same estimates with all control variables.
Unfortunately, because there was no effect on the objective measures, the null findings with respect to the content of reasoning are not particularly informative. If one were to find a large decline in partisan differences alongside no change in the content of considerations, it would be clear evidence for the misreporting explanation. However, the pair of nulls could also be explained by partisan perceptual differences being completely genuine, with no room for changes in reasoning style or incentives to misreport to affect the outcome. This alternative explanation is particularly plausible in light of the strong evidence that reasoning effort increased (Table 2).
Implications
For observers of American politics, the key implication is that even in the wake of an unusually large post-election flip in partisan economic perceptions, survey measures appear to have reflected genuine perceptual differences between Democrats and Republicans. When respondents used their assessments of economic conditions to guess the values of yet-to-be-revealed economic indicators, a $2 incentive had little or no effect on measured partisan bias, despite the success of smaller or equally sized incentives in reducing partisan differences on similar questions in past research (e.g., Bullock et al., Reference Bullock, Gerber, Hill and Huber2015; Prior et al., Reference Prior, Sood and Khanna2015; Peterson & Iyengar, Reference Peterson and Iyengar2021; Rathje et al., Reference Rathje, Roozenbeek, Van Bavel and van der Linden2023).
Although the study’s use of guesses about economic statistics to capture general economic perceptions is consistent with existing research, the results raise questions about how well this really works. On one hand, subjective measures predict objective measures about as well as the objective measures themselves, suggesting that the “signal” component of objective measures is related to general perceptions. On the other hand, these correlations were only about half as high as the between-wave correlations between the subjective measures, suggesting that there is also a considerable amount of noise in the objective measures. This is broadly consistent with Malka and Adleman’s argument that factual questions may generally fail to capture the essence of salient partisan disputes (2023, 1201). However, the results are also suggestive of question-to-question variation. Whereas the modest between-wave correlation between GDP and subjective measures was on par with the between-wave correlation between identical economic policy items in the ANES, the lower inflation and unemployment were comparable to correlations between two different ANES economic policy items (Ansolabehere et al., Reference Ansolabehere, Rodden and Snyder2008, Tables 1 and 2).
The mechanism tests using supplemental outcomes represent a small step toward a better understanding of the mechanisms at work in pay-for-correct experiments. The substantial increases in two measures of response effort, response time and looking up information (approximated by window-switching), suggest that pay-for-correct experiments affect more than misreporting. Instead, they also appear to affect how people reason, which is more consistent with the congenial inference account. Unfortunately, given the limited evidence that the treatment affected the objective measures of economic perceptions, the tests for more balanced reasoning were not informative.
In sum, this paper finds little evidence of expressive responding about the economy in the wake of Trump’s return to office, raises an important question about how well survey questions about economic statistics capture general economic perceptions, and provides evidence that the effects of pay-for-correct treatments extend to how people reason. These findings contribute a new case to the expressive responding literature and provide clues that may help advance future research.
Supplementary material
To view supplementary material for this article, please visit https://doi.org/10.1017/XPS.2025.10023
Data availability
The data, code, and any additional materials required to replicate all analyses in this article are available at the Journal of Experimental Political Science Dataverse within the Harvard Dataverse Network, at: https://doi.org/10.7910/DVN/I6SPQI.
Competing interests
The author declares none.
Ethics statement
The research was deemed exempt by the Temple University IRB (#30100). It adheres to APSA’s Principles and Guidance for Human Subjects Research. For more information on the conduct of the research see Appendix A.
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