Beliefs About the Economy are Excessively Sensitive to Household-Level Shocks: Evidence from Linked Survey and Administrative Data

What information people actually use to forecast the economy, and whether they use it correctly — answered by linking a large monthly expectations survey to a registry that records the household events in question. The framing starts from the established finding that people do not use all freely available information (Coibion and Gorodnichenko, 2012, 2015), consistent with information dispersion in Lucas (1972) and with rational inattention theories. The open question is what they do use. The paper establishes what it describes as a previously unexploited link between the Danish Consumer Expectations Survey — administered monthly by Statistics Denmark, harmonised with the European Commission’s Consumer Confidence Survey — and the Danish administrative registry, which supplies household income and assets, adverse health events and rich demographics. The paper notes in a footnote that such linkages are not yet feasible with commonly used US surveys including the Michigan Survey of Consumers, the New York Fed Survey of Consumer Expectations, the Survey of Professional Forecasters and the Blue Chip Survey.

Both compare the coefficient on a household-level variable in a regression of actual inflation against the same coefficient in a regression of forecasted inflation. Test 1 applies when the variable is plausibly in the respondent’s information set, or more generally carries no information about inflation beyond what is already there — which covers concurrently elicited survey responses, recent and salient household health events, and perhaps recent income changes. Under rational expectations the two coefficients must be identical, because the forecast error cannot be predicted by anything in the information set. Test 2′ generalises this to variables not fully inside the information set, such as realised future income changes: equality is no longer required, but “under a set of natural assumptions, the null of rational expectations requires the difference between these coefficients to be bounded by a small number, as most household-level income changes in our data are idiosyncratic.” The bounds are computed from three standard deviations — of the inflation rate (0.00361 in decimal form), of household-level income changes, and of aggregate income changes — and come to 0.02 percentage points for recent income changes and 0.042 for future income changes in the preferred specifications (0.07 and 0.087 on the longest available series). The null being rejected is deliberately broad: it “encompasses a broad class of models in which people form Bayesian forecasts using both full and potentially limited information, including rational inattention or memory constraints.”

35,050 usable responses from 2012 to 2019, plus a population registry sample of over 62 million person-years from 1991. Statistics Denmark contacts a fresh random wave of 1,500 individuals aged 16 to 74 each month from the Civil Registration System, delivering the survey through the official Digital Post system with reminders and a final telephone attempt; the average monthly response rate is 64%. The main analysis restricts to respondents aged 25 to 60 at response, to limit income changes driven by labour force entry and exit, and drops respondents with non-trivial self-employment income (not third-party reported, hence less reliable), those who declined any key forecast or backcast question, and those with missing income or demographic data. Of 55,171 respondents satisfying the age restriction, 35,050 survive the additional restrictions and the trimming of income changes at the 2.5th and 97.5th percentiles. The window 2012–2019 deliberately avoids the Great Recession and COVID-19, with every table also shown from 2008 (53,367 observations); backcast analyses drop 2012 as well, leaving 30,752 observations for 2013–2019. Recent income change is log household nominal income in year t−1 minus year t−2; future income change is year t+1 minus year t−1, where t is the survey year. Income is aggregated to the household by averaging across spouses where a spouse is present. Standard errors are clustered two ways, by calendar month and by respondent — essentially equivalent to clustering by month alone, since only 467 respondents answer more than once.

Realised inflation is unrelated to recent household income changes; inflation forecasts are strongly negatively related. In the survey sample the coefficient of realised inflation over the following twelve months on recent log nominal income change is 0.008 with a standard error of 0.022; in the population sample over 1991–2019 it is 0.034 (standard error 0.016). The corresponding forecast coefficients are −0.655 without controls, −0.674 with demographic controls (age, education, gender, number of children, and deciles of past income level), −0.563 adding calendar-month fixed effects, and −0.499 on the 2008–2019 series — all significant at the 1% level. The paper draws two conclusions: under Test 1’s assumption rational expectations require the two coefficients to be equal, “which is clearly rejected”; and even without assuming the variable is in the information set, the observed gap is an order of magnitude larger than Test 2′’s 0.02 bound. That the survey-sample and population-sample estimates of the actual-inflation coefficient are not significantly different from each other is offered as reassurance against concerns about the short time series, the smaller sample, or the period.

The paper argues not, on two grounds. The concern is that households on higher income growth trajectories might simply hold lower prior beliefs about inflation — plausible, since inflation forecasts are known to vary with income level, gender and education, which also correlate with income growth. First, adding demographic controls makes the coefficient on recent income changes larger in magnitude rather than smaller, the opposite of what a demographic-prior explanation predicts. Second, a placebo: substituting income changes from further in the past — between years t−6 and t−7, t−8, t−9 and t−10 — yields no association with inflation forecasts conditional on demographics. The authors also note the modest impact of calendar-month fixed effects implies most of the association comes from cross-sectional rather than time-series variation, which further limits concerns arising from the short series.

Robust in eleven of twelve cuts, with two identifiable exceptions. The subsamples are: income changes bounded to 20 log points in absolute value; respondents with and without employment status transitions in t−1 and t−2; respondents with neither a retirement nor a marriage transition; above- and below-median household income; college and non-college; respondents with particularly simple incomes (at least 90% labour income from t−2 to t+1); positive and negative net wealth; and public employees, whose incomes are set by the Danish Ministry of Finance and so are independent of local shocks that might drive wedges between individually experienced and national inflation. The coefficient is meaningfully lower than baseline in two cases. Respondents with some unemployment or leave in t−1 or t−2 show less association — which the paper reads as saying employment transitions do not drive the main result. And the association is lower among the college-educated, which the paper connects to findings that higher financial literacy produces more accurate inflation forecasts. Further checks: labour income rather than total income gives analogous results; real rather than nominal income changes, and net-of-tax rather than gross income, do not alter the findings; and recent changes in liquid assets and total net wealth are not strongly associated with either actual or forecasted inflation, which the authors read as consistent with those changes being less salient than income changes.

Yes, on both proxies the paper uses. First, the survey’s own question on expected change in household financial situation, on a five-point scale. The paper first establishes it carries real information: the distributions of realised future income change across the five answers are ordered almost perfectly by first-order stochastic dominance, and the difference between those answering “a lot better” and “a lot worse” is 13 log points, 0.77 of the standard deviation of income changes. Actual inflation is barely related to this response (−0.009, standard error 0.005), while forecasted inflation is strongly negatively related (−0.341 without controls, −0.320 with demographics, −0.318 controlling additionally for recent income change, −0.285 with month fixed effects). Because a survey response cannot contain information outside the respondent’s information set, Test 1 applies directly, and rational expectations are rejected. Second, realised future income changes from the tax data: actual inflation gives −0.027 (standard error 0.020) in the survey sample, while forecasts give −0.405 without controls and −0.358 with demographics, rising in magnitude to −0.445 when recent income change is also included — consistent with recent income changes being negatively related to both future income changes and forecasts. In every specification the gap far exceeds Test 2′’s 0.042 bound.

The paper addresses it two ways, one of which is a genuine within-person check. For the realised-future-income version, prior bias is argued away by the Section 3.1 placebo: any prior bias in forecasts is not associated with income growth trajectories. For the survey-based version, the paper turns to the Michigan Survey of Consumers, which asks a similar question and samples most respondents twice about six months apart (90.2% complete the follow-up in the paper’s sample). Results are similar in the Michigan data, and with respondent fixed effects included the relationship between inflation forecasts and the survey responses “is dampened, but still remains highly significant,” which the authors take as implying the excess sensitivity to news about future income is real rather than a person-level level difference.

Three things, all built on the backcast elicitation. First, inflation backcasts are strongly associated with inflation forecast errors, and inflation forecasts are strongly associated with backcast errors — by Test 1 neither is consistent with rational expectations, and together the authors read them as showing that memory is imperfect and perceptions of the past are biased. Second, running the Section 3 regressions with backcasts in place of forecasts reproduces the results, and more strongly: realised past inflation is unrelated to all three income measures, but backcasts are significantly negatively associated with them (−0.862 for recent income changes with demographic controls, −0.312 for the family finances forecast, −0.510 for realised future income changes). Pooling forecast and backcast elicitations and interacting each income measure with forecast/backcast indicators, the ratio of backcast to forecast coefficient is above one for all three measures. Third, and the part that distinguishes mediation from mere differential sensitivity: adding backcasts as a covariate significantly attenuates the coefficients on the income measures — “significantly dampened, or even statistically indistinguishable from zero” — with the difference significant at p < 0.01 in each of the three pairs of regressions. The paper is explicit that the second fact alone would not rule out a model in which income changes simply receive more weight for past than future inflation, and constructs the third test precisely to discriminate.

Three specific alternative readings. They reject the standard macroeconomic assumption that people have full knowledge of recent inflation — if they did, reports of past inflation, noisy or not, would not be related to income changes. They reject the hypothesis that people have imperfect memory but use their recalled information in a Bayesian way, a “sophistication” assumption made in a range of theoretical work on imperfect memory. And the backcast results for future income measures reject the possibility that respondents simply do not understand the word inflation and answer as if asked about their purchasing power: positive future income changes raise future purchasing power but cannot affect past purchasing power, so that reading cannot explain a negative association between backcasts and expected future income.

By supplying a negative household event with no connection to prices at all, whose timing relative to the survey is random. The comparison is between two respondents with the same number of family emergency-room visits over the sample period and the same demographics, one of whom happened to be contacted in the month of a visit — random, because Statistics Denmark draws a fresh sample each month. The paper lists why these visits suit the test: they plausibly proxy for negative events producing negative affect; they are plainly unrelated to inflation; they are common enough to give statistical power while controlling for a household’s general propensity to visit; and because emergency care is free in Denmark, a visit conveys no price information. The data cover 2008–2018 (the registry changed reporting system in 2019), and the demographic restrictions of the main analysis are dropped, since there is no reason for the relationship to differ by labour force status. Households average 3 visits over the period and 0.19 in the survey month; 90% have seven or fewer, and households with eight or more are excluded, on the reasoning that for them a visit is less unusual and hence less affect-inducing, and because extreme counts reduce power. Results: a significant and robust effect of a visit in the survey month on pooled backcasts and forecasts, of roughly 0.2 percentage points, about five times larger than the 0.045 association with one additional visit anywhere in the sample period; unchanged when controlling for total visits quadratically or with fixed effects interacted with age; and, if anything, slightly larger when recent and future income changes are controlled for, which rules out the income measures mediating it. As with income, the effect is larger on backcasts than on forecasts. The main threat the authors consider is differential non-response, which they address directly: a visit reduces survey completion by about 0.010 and insignificantly, and for attrition to generate the observed effect the marginal dropouts would need forecasts and backcasts about 12.8 percentage points below average — which they call implausible, and still more so for the asymmetry between backcasts and forecasts.

A memory model in which the probability of recalling a past inflation state is reweighted by how closely its affective valence matches the affect of the current cue — and it generates a testable prediction the data bear out. Recall probabilities are tilted by a similarity function with intensity parameter θ; at θ = 0 the model is Bayesian. Backcasts and forecasts then equal the Bayesian estimates minus a term proportional to the affect induced by the cue, with the sensitivity weight increasing in θ and decreasing in the precision of the person’s information about past inflation. Two implications matter. First, because past inflation informs future inflation only partially, the forecast coefficient is a fraction of the backcast coefficient — which delivers the observed ordering rather than assuming it. Second, people with more precise information should be less influenced by affect, “which is consistent with our results that there is less excess sensitivity among the college-educated.” The paper states the structural debt and the limit plainly: the model largely follows the associative-memory framework of Bordalo and co-authors, with affect replacing representativeness in the similarity function; θ is not identified without an estimate of information precision, since the sensitivity weight could be zero either because θ is zero or because knowledge of the past is perfect; and it assumes the person does not fully account for how affect distorts recall, since someone who did would not violate the tests.

Direct evidence for the model’s two assumptions, from fresh samples in Denmark and the United States. The survey was fielded in Denmark in May and June 2025 — 22,521 invitations via Digital Post, 3,744 complete submissions, entered in a raffle for ten prizes of 1,000 Danish kroner — and in the US on Prolific Academic in October 2024, 1,600 submissions sampled to be representative of the Census on age, gender and ethnicity, paid $2, of which 1,523 remained after dropping 77 who failed an attention check. Three findings. First, household-level experiences shape inflation forecasts about as much as macroeconomic factors: the probability a macroeconomic factor is rated as mattering “a lot” is 0.16 in Denmark and 0.24 in the US, against 0.18 and 0.27 for household-level factors; “change in price of groceries” receives the highest mean rating of all factors in both samples, while money supply and monetary policy rank lowest among the macroeconomic options. “Feeling financially strained” ranks fourth among household factors, with scores comparable to household spending, oil and energy prices, and supply chain conditions. Second, cues whose affective valence matches the valence of the experience being recalled are significantly more likely to be selected as influencing recall “a lot” — by 94% for financial and 137% for non-financial cues in Denmark, and 188% and 267% in the US. Third, the same holds specifically for recall of inflation episodes: congruent cues raise selection by 33% (financial) and 52% (non-financial) in Denmark, and 74% and 74% in the US. The paper also verifies the assumption that inflation carries negative affect: 66% of Danish and 87% of US respondents rated price increases as unpleasant, and the effects are concentrated among those who do.

Four, each rejected on a specific pattern rather than in general terms. Overconfidence or over-precision cannot explain the greater sensitivity of backcasts, nor sensitivity to events completely idiosyncratic to inflation such as emergency-room visits; and the magnitudes are out of reach — the lower bound of the 95% interval on the actual-inflation coefficient is about −0.04 while the upper bound on the forecast coefficient is about −0.40, so people would have to overweight the informational content of income changes “by at least a factor of 10, a degree of overreaction far larger than is typically estimated or assumed in these models.” A “supply-side” view of inflation, in which people see inflation as driven by negative supply shocks that also cut their income, explains the sign but not the magnitude of the gap: the appendix shows that misperceiving the sign of the correlation can loosen the test bound by at most twice the actual-inflation coefficient, which is negligible — and it explains neither the health-shock results nor the mediating role of memory. Affective association without memory, in the form of a “what you see is all there is” binary good/bad categorisation, does not explain why backcasts are more sensitive than forecasts or why controlling for backcasts attenuates the forecast relationship. Finally, respondents reporting some quantile of their belief distribution other than the mean cannot explain the emergency-room results or the memory mediation, and would require the reported quantity to be more than ten times as sensitive to information as the mean, for which the authors say they know of no natural assumption.

Two, both stated as implications rather than demonstrated here. First, the mechanism can amplify the macroeconomic impact of aggregate shocks: an accommodative monetary or fiscal shock raises household income, which makes people more optimistic about the economy, which raises spending further, which reinforces confidence — the paper identifies this as the “confidence multiplier” of Akerlof and Shiller (2010) and Angeletos and Lian (2022). Second, citing Broer et al. (2025), differences in beliefs driven by idiosyncratic shocks produce differences in consumption and saving that shape the wealth distribution, and the paper’s contribution is to show how affect-cued recall generates those belief differences. The conclusion also frames the challenge as extending beyond rational expectations “to a variety of ‘quasi-Bayesian’ models in behavioral economics,” suggests existing “experience effects” findings may reflect a broader psychology not limited to within-domain extrapolation or realised past experiences, and speculates that policies improving wellbeing may generate economic spillovers through the affect channel — with the explicit caveat that documenting how affect-cued recall affects actual decisions is left to future work.