On the controllability of evaluative-priming effects: Some limits that are none

Abstract

Two experiments examined recent claims of uncontrollability of the evaluative-priming effect. According to these claims, imposing an adaptive 600 ms response deadline prevents successful faking (Degner, 2009). Furthermore, strategic control attempts have been argued not to reduce the priming measure's sensitivity to spontaneous evaluations so that correlations of evaluative-priming effects with external criteria are not affected by attempts to fake (Bar-Anan, 2010). Here, we show that faking is possible even with an adaptive 600 ms response deadline when faking instructions do not conflict with speed pressures imposed thereby (Experiments 1 and 2). In addition, suitable faking instructions substantially affect the predictive validity of priming effects in terms of their correlations with (non-faked) self-report measures and the Implicit Association Test (Experiment 2). The previous claims about the uncontrollability of the evaluative-priming effect may thus have been premature.

Keywords:

• Evaluative priming
• Implicit measures
• Faking
• Strategic effects
• Automaticity

Acknowledgments

The research reported in this paper was supported by Grant Kl 614/31–1 from the Deutsche Forschungsgemeinschaft to Karl Christoph Klauer.

We wish to thank Christine Örtl, Benedikt Hopfinger, Irene Reinhardt, and Melanie Bienert for their help in collecting data.

Notes

¹For the sake of brevity, we do not report these results in detail here. Note, however, that results were the same as in Experiments 1 and 2.

²Note that the direct comparison of Degner's and our response deadline condition required confounding the factor response deadline and the factor adaptive procedure. However, this confounding appears to be negligible given that the adaptive nature of the 600 ms response deadline condition had little impact on both the actual response deadline (that remained at 600 ms for most participants) and the results, as is detailed in the general discussion.

³All materials can be obtained from the first author.

⁴Note that providing participants with idiosyncratic faking strategies does not guarantee that the same cognitive processes are activated in participants who prefer the same attitude object. Of course, several moderating variables such as motivation, cognitive resources, or extremity of the attitude, among others, might influence the actually applied cognitive strategy.

⁵Less interesting for the present research question, the interaction of Prime Type and Consistency, F(1, 97) = 26.33, p<.001, , the interaction of Prime Type and Faking, F(1, 97) = 5.63, p=.02, , and the main effect of Consistency, F(1, 97) = 24.80, p<.001, , reached significance, whereas the main effect of Prime Type only approached significance, F(1, 97) = 3.72, p=.06, . No other effects were significant, Fs ≤ 1.28, ps≥.26.

⁶Note that we also re-ran all correlation analyses after excluding bivariate outliers. Following Bar-Anan (2010), outliers were identified by computing two outlier indices per correlation and participant: Participants with a Cook's D value above the threshold of the relevant sample size and/or with an absolute studentised residual larger than two were excluded. Importantly, analyses without bivariate outliers revealed the same pattern of significant and non-significant results as analyses including all participants.

⁷Again, analyses without bivariate outliers revealed the same pattern of significant and non-significant results as analyses including all participants.

⁸More precisely, we conducted further analyses in order to understand why the significant correlations in the CG in the analyses across both subgroups turned into zero correlations in the analyses separately for each subgroup. Our idea was that external correlations of the evaluative-priming effect must be mainly driven by information about their direction, that is, the sign of the effect. If this was true, the rank orders within each subgroup of Greens voters versus CDU voters would not be informative regarding the attitude in question because valid information about spontaneous prime evaluations is assumed to be reflected only in the sign of the priming effect (i.e., a constant of −1 or +1). Such restrictions of construct variance would lead to the present correlation pattern of zero correlations within each subgroup and substantial correlations across both subgroups. Furthermore, this idea could explain why implicit–explicit correlations were significantly reversed in the EG: If valid information about the attitude in question is only reflected in the sign that EG members are able to reverse, then this should lead to significantly reversed external correlations.

We therefore repeated all correlation analyses with evaluative-priming scores recoded to −1 or +1, depending on their sign. Confirming our explanation, external correlations of the sign-recoded evaluative-priming effects were the same as those of the original (untransformed) evaluative-priming effects, ∣Z∣<1.55, p>.12. Furthermore, repeating the moderated regression analyses reported above with the sign-recoded evaluative-priming effects revealed the same pattern of significances as the analyses using the original evaluative-priming effects. It can thus be concluded that external correlations of the evaluative-priming effect were mainly driven by information about the sign.

Note that this result pattern is not specific to our data. For instance, re-analyses of Bar-Anan's (2010) data also revealed that external correlations of evaluative-priming effects were mainly based on inter-individual differences in the signs, not in the sizes of priming effects, leading to considerably reduced external correlations of evaluative-priming scores, when subgroups with constant attitude directions were considered. We thank Yoav Bar-Anan for providing us with the data sets of the five experiments.