What 31 Datasets Reveal—and What They Do Not
Here the subject is the published evidence for naturally occurring, longitudinal contact–attitude change. The focus is what happens when the same datasets are analyzed with models that treat stable differences between people and changes within people differently. The result gives the reader a more defensible judgment than either headline—“contact causes better attitudes” or “contact has no effect”—because it shows exactly which part of the signal survives and which part becomes uncertain.
A deliberately broad but bounded re-analysis
The researchers began with a systematic search rather than a convenient selection of famous studies. In October 2022, they searched PsycINFO, PsycARTICLES, and PSYINDEX for combinations of intergroup contact and longitudinal research, then checked the cited literature of the studies they found. The search identified 145 longitudinal contact studies. To enter the re-analysis, a study had to measure direct intergroup contact at the individual level, include an outgroup attitude or a related outcome for which contact theory supplied a meaningful prediction, contain at least three measurement waves, include at least 100 participants, omit a contact intervention, and be a peer-reviewed English-language publication available before October 2022.
Those conditions serve the comparison, but they also define its limits. At least three waves were needed because the full-forward and random-intercept models require more than two measurement points. Excluding interventions kept the question focused on naturalistic contact rather than mixing designed treatment effects with everyday exposure. Requiring a theoretically interpretable outcome avoided treating any variable that happened to correlate with contact as an attitude effect. These are sensible boundaries, but they mean the database is not a census of every contact study and is not a direct test of the virtual program examined later.
Twenty-six publications met the formal inclusion criteria. The authors obtained data from 17 publications and reconstructed variance–covariance information from four more using reported item correlations and standard deviations. The final analysis covered 31 datasets from 21 publications and 33,348 participants. It included population-representative and convenience samples, adults and students, adolescents and a parent–child dyad, and groups situated in Asian, African, European, Latin and North American, and Oceanian contexts. Contact was measured in several ways: general or positive and negative contact, friendship networks, numbers of intergroup friends, roommates, and romantic partners. Attitudes likewise ranged from warmth and prejudice to general evaluation, trust, anxiety, tolerance, and related outcomes.
That heterogeneity makes the re-analysis useful and difficult. It makes the central pattern less dependent on one age group, one country, or one operational definition. But it also means that a model comparison is being repeated across different exposure types, intervals, samples, and outcomes. A single percentage of significant paths should therefore be read as a description of the assembled tests, not as the probability that a randomly chosen person will change by a particular amount.
The measures themselves define what “contact” means in each test. A count of outgroup friends captures an opportunity structure and a social network; a rating of positive or negative encounters captures a participant’s evaluation of contact; a roommate or romantic-partner indicator marks a more sustained relationship. The outcome may be warmth, trust, prejudice, anxiety, tolerance, or an approach tendency. These variables can be related, but they are not interchangeable manifestations of one scale. A model may be asking whether a new friendship matters, whether the frequency of ordinary encounters matters, or whether people who live in different social environments differ in their attitudes. Treating all of them as the same exposure would hide the very design choices that the re-analysis is meant to expose.
The database’s breadth also should not be confused with equal evidentiary strength. Some analyses used original participant data, while others used reported covariance information; the authors tried to follow the original exclusions and measures but made documented deviations when the available data required them. Several study characteristics were imbalanced, and the re-analysis was too small to determine whether age, group status, context, or interval systematically moderated the results. The comparison is therefore strongest as a demonstration of sensitivity across plausible analyses, not as a precise ranking of every kind of contact experience.
The first surprise is the mismatch between model fit and apparent theoretical support. The conventional cross-lagged panel model often failed to represent the observed data adequately. Among the freely estimated CLPMs, none of 20 had adequate fit on all three indicators; among the stationarity versions, only one of 11 did. Yet the freely estimated CLPM produced significant cross-lagged effects in the direction predicted by contact theory in 56 of 142 tests, or 39.4 percent. Under stationarity assumptions, the share was 44 of 65, or 67.7 percent. A model can therefore return many theory-consistent paths while also failing to describe the observed variance and covariance structure well.
This is not a technical footnote about whether a statistical package accepts the model. Poor fit means that the model’s restrictions do not line up well with the relationships visible in the data. In that situation, a significant contact-to-attitude path is being read inside a representation that is already missing or misdescribing important structure. The path may still contain information, but its causal interpretation carries the model’s failure along with it. Conversely, a model that fits better earns a more credible description of the data, not an automatic license to call its preferred path causal.
The full-forward model does not solve the problem by offering a more attractive fit statistic. Because it freely estimates all possible structural paths, it is just-identified and has perfect fit by construction. The relevant comparison is its last-interval cross-lag, where prior exposure is more extensively represented. Those effects supported contact theory in about one-third of the examined cases, a lower share than the conventional model and not enough to produce a significant average in the internal meta-analysis.
The random-intercept model fit the data more comfortably: 16 of 19 freely estimated models had adequate fit, as did all 12 stationarity models, and fit improved over the conventional model in every direct comparison. But its theory-relevant within-person paths were significant in only about one case in eight. The stable between-person contact–attitude correlations told a different story, supporting contact theory in 32 of 47 freely estimated cases and 17 of 27 stationary cases. Two random-intercept models also produced implausible parameter estimates, a reminder that better average fit does not eliminate estimation problems.
The signal that survives—and the uncertainty around it
The internal meta-analysis makes the model contrast more precise. For non-valenced or positive contact, the average Fisher r-to-z coefficient in the freely estimated CLPM was 0.0538, with a 95 percent confidence interval from 0.0324 to 0.0753. It was statistically significant. The corresponding FF-CLPM estimate was 0.0191, with a confidence interval from −0.0262 to 0.0645, and the RI-CLPM within-person estimate was 0.0078, with a confidence interval from −0.0057 to 0.0212. Neither stronger-controlled longitudinal estimate was statistically significant. Meanwhile, the RI-CLPM between-person estimate was 0.3144, clearly positive and much larger in magnitude. The stable association is therefore not an incidental remnant; it is a substantial pattern that answers a different question from whether a person changes after their contact changes.
Negative contact follows the same inferential shape with the expected sign. The freely estimated CLPM produced an average coefficient of −0.0596, with a confidence interval from −0.1024 to −0.0168. The FF-CLPM estimate was −0.0409, with a confidence interval that included zero, and the RI-CLPM within-person estimate was −0.0281, also not statistically significant. The random-intercept between-person estimate was −0.3282 and statistically significant. Thus, people who differ in their enduring levels of negative contact can also differ in their attitudes in the predicted direction, while the evidence that a person’s own increase in negative contact subsequently changes their attitude is less secure under the stronger-controlled models.
These coefficients are Fisher-transformed correlations, not percentage-point changes on an attitude thermometer. Their value in this comparison is diagnostic: the positive and negative patterns both weaken when the analysis asks more explicitly about within-person longitudinal change and stable confounding. The result is not that contact and attitudes are unrelated. It is that a relationship observed between people can be large even when the estimated within-person temporal effect is small and uncertain.
The averages also conceal considerable variation. Heterogeneity tests were highly significant for every model and valence grouping. The contributing studies differed in the length of the interval between measurements, the total study period, the way contact was measured, the attitude outcome, the population, and the social context. A six-week interval may capture a different process from a two-year interval. A friendship nomination is not interchangeable with a single rating of positive contact, and a warmth thermometer is not interchangeable with avoidance or trust. The re-analysis shows that the statistical model matters, but it also shows that study design features matter alongside it.
Power adds a second reason to resist a simple reading of the null within-person results. The retrospective power analysis found very low power below 1,000 participants. For the small effects commonly observed in this literature, roughly 80 percent power required samples above 2,000 for the CLPM and full-forward model and substantially larger samples for the random-intercept model. Only about one-quarter of the re-analyzed datasets appeared sufficiently powered to detect effects of the relevant size. A non-significant estimate in a small panel may therefore reflect a small effect that the design could not detect, as well as a genuinely absent effect.
Timing creates a related problem. Naturalistic studies usually observe habitual contact—ordinary fluctuations in an already established social environment. Those changes may be too small to produce a detectable attitude shift, or the measurement wave may arrive after a short-lived response has faded. The authors suggest that first contact, a major transition such as entering a new institution, or a sharp rupture in contact could produce a larger effect than routine variation. The database was not large or balanced enough to test those possibilities systematically.
Finally, stronger control is not the same as certainty. The three models represent only a small part of the available longitudinal toolkit, and each relies on assumptions about how the data were generated. The authors could not recover every eligible dataset because of non-response or unavailable data, and the inclusion rules favored published English-language evidence. Their conclusion is consequently carefully bounded: conventional CLPM results provide longitudinal evidence in line with contact theory, but those effects are questionable when the model fits poorly and fails to separate stable differences. The stronger-controlled models provide little evidence of a general naturalistic within-person effect in this database, while leaving open the possibility of small, time-sensitive, context-dependent changes.
The most informative next evidence would not come from simply adding another routine survey wave. It would come from matching measurement to the proposed process: following people through first contact or a major transition, measuring short-term and longer-term responses, and collecting enough participants to distinguish modest effects from noise. Larger and more balanced datasets could also test whether age, group status, the salience of group boundaries, context, or the length of the interval changes the result. In parallel, well-designed experiments could provide the counterfactual that naturalistic panels lack, while longitudinal follow-up could show whether an intervention’s initial effect persists in ordinary life. The re-analysis therefore points toward triangulation rather than a single victorious model.
That is a narrower conclusion than “contact does not work,” and a more useful one. The re-analysis tests ordinary survey fluctuations, not a well-supported contact intervention. It tells us that the causal-looking signal in naturalistic panels is sensitive to how person-level variation is handled. To learn what evidence looks like when contact is intentionally structured and repeatedly supported, we need a field case built around a different design logic.