Sp 2016 47 issue 1

Volume 47 / Number 1 / 2016

Volume 47 / Number 1 / 2016

Social Psychology

Social Psychology

Editor-in-Chief Christian Unkelbach Associate Editors Julia Becker Malte Friese Michael Häfner Hans J. IJzerman Markus Kemmelmeier Ulrich Kühnen Ruth Mayo Michaela Wänke

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17.12.2015 09:57:42

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Social Psychology

Volume 47, No. 1, 2016

Editor-in-Chief

Christian Unkelbach, Department of Psychology, Universita¨t zu Ko¨ln, Richard-Strauss-Str. 2, D-50931 Cologne, Germany, Tel. +49 221 470-2001, E-Mail christian.unkelbach@uni-koeln.de

Editorial Office

Juliane Burghardt, Department of Psychology, Universita¨t zu Ko¨ln, Richard-Strauss-Str. 2, D-50931 Cologne, Germany, Tel. +49 221 470-7108, E-Mail Social-Psychology@uni-koeln.de

Associate Editors

Julia Becker, Universita¨t Osnabru¨ck, Germany Malte Friese, Universita¨t des Saarlandes, Germany MichaelHa¨fner,Universita¨tderKu¨nsteBerlin,Germany Hans IJzerman, Vrije Universiteit Amsterdam, The Netherlands

Markus Kemmelmeier, Univ. of Nevada at Reno, USA Ulrich Ku¨hnen, Jacobs University, Germany Ruth Mayo, Hebrew University of Jerusalem, Israel Michaela Wa¨nke, Universita¨t Mannheim, Germany

Consulting Editors

Susanne Abele (Oxford, OH, USA) Andrea Abele-Brehm (Erlangen-Nu¨rnberg, Germany) Herbert Bless (Mannheim, Germany) Gerd Bohner (Bielefeld, Germany) Rupert J. Brown (Sussex, Brighton, UK) Olivier Corneille (Louvain, Belgium) Juliane Degner (Hamburg, Germany) Amanda Diekman (Oxford, OH, USA) Alice H. Eagly (Evanston, IL, USA) Gerald Echterhoff (Mu¨nster, Germany) Birte Englich (Cologne, Germany) Hans-Peter Erb (Hamburg, Germany) Jens Fo¨rster (Amsterdam, The Netherlands) Bertram Gawronski (Austin, TX, USA) Guido Gendolla (Geneva, Switzerland) Roberto Gonza´lez (Santiago, Chile) Bettina Hannover (Berlin, Germany) Guido Hertel (Mu¨nster, Germany) Kurt Hugenberg (Oxford, OH, USA) Franciska Krings (Lausanne, Switzerland) Thorsten Meiser (Mannheim, Germany) Thomas Morton (Exeter, UK) Gabriel Mugny (Geneva, Switzerland)

Thomas Mussweiler (Cologne, Germany) Roland Neumann (Trier, Germany) Paula Niedenthal (Clermont-Ferrand, France) Henning Plessner (Heidelberg, Germany) Marc-Andre´ Reinhard (Mannheim, Germany) Astrid Schu¨tz (Bamberg, Germany) Stefan Schulz-Hardt (Go¨ttingen, Germany) Sabine Sczesny (Bern, Switzerland) Margaret Shih (Los Angeles, CA, USA) Frank Siebler (Tromsø, Norway) Monika Sieverding (Heidelberg, Germany) Paul Silvia (Greensboro, NC, USA) Siegfried Sporer (Gießen, Germany) Dagmar Stahlberg (Mannheim, Germany) Fritz Strack (Wu¨rzburg, Germany) Rolf van Dick (Frankfurt/Main, Germany) G. Tendayi Viki (Canterbury, UK) Ulrich Wagner (Marburg, Germany) Eva Walther (Trier, Germany) Michael Wohl (Ottawa, ON, Canada) Bogdan Wojciszke (Warsaw, Poland) Rex A. Wright (Birmingham, AL, USA) Vincent Yzerbyt (Louvain-la-Neuve, Belgium)

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Ó 2016 Hogrefe Publishing. This journal as well as the individual contributions and illustrations contained within it are protected under international copyright law. No part of this publication may be reproduced, stored in a retrieval system, or transmitted, in any form or by any means, electronic, mechanical, photocopying, microfilming, recording or otherwise, without prior written permission from the publisher. All rights, including translation rights, reserved.

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Impact Factor (2014): 1.662

Social Psychology 2016; Vol. 47(1)

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Contents Editorial

Increasing Replicability Christian Unkelbach

1

Original Articles

The Effects of Invoking Stereotype Excuses on Perceivers’ Character Trait Inferences and Performance Attributions Jade S. Jenkins and John J. Skowronski

4

Preaching to, or Beyond, the Choir: The Politicizing Effects of Fitting Value-Identity Communication in Ideologically Heterogeneous Groups Maja Kutlaca, Martijn Van Zomeren, and Kai Epstude

15

Do I Shoot Faster Because I Am Thinking about an Outgroup or a Threatening Outgroup? Shooter Bias, Perceived Threat, and Intergroup Processes Jessica Mange, Keren Sharvit, Nicolas Margas, and Ce´cile Se´ne´meaud

29

The Validity of Crowdsourcing Data in Studying Anger and Aggressive Behavior: A Comparison of Online and Laboratory Data Johannes Lutz

38

Heart Versus Mind: How Affective and Cognitive Message Frames Change Attitudes Fabian A. Ryffel and Werner Wirth

52

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Social Psychology 2016; Vol. 47(1)

Editorial Increasing Replicability Christian Unkelbach Department of Psychology, Universität zu Köln, Germany

Over the last four years (Unkelbach, 2013–2015), I used the editorials to keep readers updated on the proceedings behind the scenes, to inform about important changes, and to provide authors with information about impact and turnaround rates. From this informational perspective, this will be an atypical editorial, as I will almost solely address how Social Psychology as a journal might contribute to a better social psychological science by increasing the replicability of the results published within our pages. This is a somewhat personal view, but informed by recent publications on the topic and by the experiences as Editor-in-Chief of Social Psychology.

Replicable Social Psychological Science In October 2015, Brian Nosek and 270 contributing authors published an article in Science (Open Science Collaboration, 2015) that attempted to replicate 100 psychological experiments from high-profile outlets. This article had its predecessor in Social Psychology with our Registered Reports Special Issue on replications (Nosek & Lakens, 2014); in this special issue, authors preregistered their replication attempts of classic and contemporary findings.

Some classic findings replicated (e.g., Wesselmann et al., 2014), while others did not (Nauts, Langner, Huijsmans, Vonk, & Wigboldus, 2014), and there was a lively debate captured in the comments on this issue and the respective rejoinders (e.g., Monin & Oppenheimer, 2014; Schwarz & Strack, 2014). The recent 100 experiments Science article used only published experiments from 2008. It came up with a rate of 36 significant results in the direction of the original findings. The debate about the implications of the specific numbers and the reasons for successes and failures of these attempts has taken place elsewhere (see, e.g., Maxwell, Lau, & Howard, 2015; Stroebe & Strack, 2014).

Yet, a trend is visible: published psychological experiments seem to be not easy to replicate. In the following, I want to

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discuss how we might increase replicability of research results published in Social Psychology.

What Have We Done, How Are We Doing, and What Will be Done In 2013, we announced and started ‘‘Replications’’ as a submission category, based on the belief that ‘‘our discipline should acknowledge the value of replications and honor researchers’ time and investments in replication attempts by providing space to publish these attempts’’ (Unkelbach, 2013, p. 2). And as stated above, in 2014, we published the Registered Reports Replication Special Issue. This early focus on issues of replicability has strongly influenced the editorial team and its decisions within the last years.

This influence is visible from Ulrich Schimmack’s blog on replicability (Replicability, 2015). The blog provides a ranking of research journals in psychology based on the post hoc computed replicability of the published results.

The resulting index of replicability is based on the observed median power and the percentage of significant results. It is assumed to provide a probability for replicating a given significant result with the same procedures, materials, and sample size. Given this index, Social Psychology as a journal is ranked no. 9 out of 54 journals based on articles published in 2015. This makes Social Psychology the highest ranking social psychological journal within the list. Please note that there are many explanations for how the index comes about and I am very hesitant to interpret such rankings; however, it indicates that articles published in Social Psychology have adequate (albeit not good) power, and there is an upward trend (i.e., the average index has increased from 0.62 for papers published within 2010 to 2014, to 0.71 for papers published in 2015 with a 95% confidence interval from 0.62 to 0.78).

The question is how to enhance the replicability of our results further. I will address three basic points that researchers, reviewers, and editors who contribute to Social

Social Psychology 2016; Vol. 47(1):1–3 DOI: 10.1027/1864-9335/a000270

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Editorial

Psychology should keep in mind (and I am sorry if I may be repeating the obvious here). For sure, I can only scratch the surface, but I hope it gets the gist across how I believe one might increase replicability.

n = 32 and does not increase with more participants (see Westfall et al., 2015, Figure 1); in other words, increasing the sample of participants does not further increase power if the sample of stimuli is not increased as well. Thus, stimulus sampling allows generalizations and increases power, which increases replicability.

Increase N The call for increasing sample sizes is very prominent, and there are many sources detailing the necessity of larger participant samples in psychological research. Among other advantages, larger samples increase the probability to detect a hypothesized effect if it exists, larger samples provide more precise estimates of an effect, and larger samples provide more confidence in the nonexistence of an effect given a null result. Thus, a result based on large n is less likely to be a false positive result and should therefore be more likely to replicate; this is particularly true if one does not only investigate experimental, but also correlational results (see Schönbrodt & Perugini, 2013). However, large samples are also among the most costly endeavors. But there are other ways to increase replicability.

Sample Stimuli Wells and Windschitl (1999) discussed a pervasive problem in social psychological research. Most experiments sample participants but do not sample stimuli. Their illustrative example involves a hypothetical hitchhiking experiment in which a woman or a man holds out her/his thumb a hundred times and the dependent variable is how often she/he gets a ride.

The hypothetical result is that the woman gets significant more rides than the man, leading to the false conclusion that women get more rides than men as hitchhikers. However, the design only allows concluding that this specific woman gets more rides than this specific man. To make claims for women and men, one needs to sample stimuli from these categories the same way one samples participants from a population.

Judd, Westfall, and Kenny (2012; see also Westfall, Kenny, & Judd, 2014) explored another aspect of this problem. Lack of stimulus sampling inflates Type I error probability for an effect because variation due to the stimuli is ascribed to the experimental variations by standard ANOVAs. The authors provide all the necessary syntax to avoid this inflated error probability by analyzing stimuli and participants simultaneously in mixed model analyses.

However, for the present argument, the two most important aspects are that (a) not sampling stimuli does not allow generalization and thereby hinders successful replication beyond the stimuli used in the to-be-replicated study, and (b) not sampling stimuli stunts increases in power when n is increased (Westfall, Judd, & Kenny, 2015, p. 394).

In fact, if stimuli account for 30% of the variance in a given dependent variable, effective power levels out around

1

Derive Clear Predictions Reading a scientific journal is in many respects like reading a normal journal; and journals are expected to provide exciting and surprising facts and news. However, exciting and surprising results are almost by definition unlikely, that is, it is most likely false a priori (see Ioannidis, 2005); importantly, a significant result (i.e., p < .05) does not increase the chances much that an effect is real if it is highly unlikely a priori (Nuzzo, 2014). Strong claims (i.e., unlikely findings) need strong support. In other words, replicating an unlikely result is also an attempt that is unlikely to succeed a priori. The likelihood that an effect exists is unfortunately difficult to assess directly in advance, but theoretical clarity makes for a good proxy. If a theory is based on well-grounded assumptions, a likely outcome is one that is clearly predicted by the theory. Thus, to increase replicability, effects need to be clearly theoretically derived, although this might make for less exciting reading sometimes. However, the true beauty of a hypothesis might emerge if plausible assumptions are combined to lead to surprising, but nevertheless clear predictions.1

Concrete Measures These three basic points are rather abstract, but as a general guideline for authors, reviewers, and editors, it is clear that we want to publish studies that have predictions clearly derived from theories which are tested with large samples of participants and samples of stimuli. On the more concrete level, we will implement the by now standard measures that might increase replicability by urging authors to (a) report sample size and power considerations, (b) report effect sizes and confidence intervals for these effect sizes, (c) to share their data, (d) to share their materials, and (e) to preregister experiments. While (a) and (b) are easily implemented and will be required, (c)–(e) will be by choice and based on an incentive system; that is, as already done in our Registered Reports Special Issue, we will start awarding badges for articles for which data and materials are openly accessible and in the best case, for which the underlying research was preregistered. I hope that both these abstract and concrete points further help that, as I already stated in 2013, Social Psychology as a journal contributes to a more solid foundation of social psychological research.

Please note that this point is the opposite of hypothesizing after the effects are known (i.e., HARKing; Kerr, 1998). Such a practice actively reduces the replicability, because possible chance findings (i.e., false positives) are disguised as theoretically-derived.

Social Psychology 2016; Vol. 47(1):1–3

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Editorial

Closing Remarks These thoughts on replicability come for me at the end of my 4-year term as editor-in-chief. And given this end of my tenure, I sincerely want to thank the associate editors who worked for the journal during the last 4 years for their contribution to Social Psychology. Without the input and effort of Julia Becker, Juliane Degner, Roland Deutsch, Gerald Echterhoff, Hans-Peter Erb, Malte Friese, Michael Häfner, Hans IJzerman, Eva Jonas, Markus Kemmelmeier, Ulrich Kühnen, Alison Ledgerwood, Ruth Mayo, Margaret Shih, Nicole Tausch, and Michaela Wänke, the journal would not be in the good shape it is now. And most importantly, I want to thank Juliane Burghardt for her invaluable help and her management of the editorial office of Social Psychology: Merci, Juliane!

The last bit of information is that the new incoming editor-in-chief, as of April 1, 2016, will be Kai Epstude from the University of Groningen. Welcome Kai, and all the best for your term as editor and for the journal!

References Ioannidis, J. P. A. (2005). Why most published research findings are false. PLoS Medicine, 2, e124.

Judd, C. M., Westfall, J., & Kenny, D. A. (2012). Treating stimuli as a random factor in social psychology: A new and comprehensive solution to a pervasive but largely ignored problem. Journal of Personality and Social Psychology, 103, 54–69.

Kerr, N. L. (1998). HARKing: Hypothesizing after the results are known. Personality and Social Psychology Review, 2, 196–217.

Maxwell, S. E., Lau, M. Y., & Howard, G. S. (2015). Is psychology suffering from a replication crisis? What does ‘‘failure to replicate’’ really mean? American Psychologist, 70, 487–498.

Monin, B., & Oppenheimer, D. (2014). Commentaries and rejoinder on Klein et al. (2014): The limits of direct replications and the virtues of stimulus sampling. Social Psychology, 45, 299–301. doi: 10.1027/1864-9335/a000202 Nauts, S., Langner, O., Huijsmans, I., Vonk, R., & Wigboldus, D. J. (2014). Forming impressions of personality: A replication and review of Asch’s (1946) evidence for a primacy-of-warmth effect in impression formation. Social Psychology, 45, 153–163. doi: 10.1027/1864-335/a000179 Nosek, B. A., & Lakens, D. (2014). Registered reports: A method to increase the credibility of published results.

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Social Psychology, 45, 137–141. doi: 10.1027/1864-335/ a000192 Nuzzo, R. (2014). Statistical Errors. Nature, 506, 151–153.

Open Science Collaboration. (2015). Estimating the reproducibility of psychological science. Science, 349, 943.

Replication-Index. (2015). Replicability Ranking of 54 Psychology Journals. Retrieved from https://replicationindex. wordpress.com/2015/10/27/2015-replicability-ranking-of54-psychology-journals/ Schönbrodt, F. D., & Perugini, M. (2013). At what sample size do correlations stabilize? Journal of Research in Personality, 47, 609–612.

Schwarz, N., & Strack, F. (2014). Does merely going through the same moves make for a ‘‘Direct’’ Replication? Concepts, contexts, and operationalizations. Social Psychology, 45, 305–306. doi: 10.1027/1864-9335/a000202 Stroebe, W., & Strack, F. (2014). The alleged crisis and the illusion of exact replication. Perspectives on Psychological Science, 9, 59–71.

Unkelbach, C. (2013). Social Psychology – change and consistency. Social Psychology, 44, 1–3. doi: 10.1027/1864-335/ a000135 Unkelbach, C. (2014). The best of times, the worst of times.

Social Psychology, 45, 71–73. doi: 10.1027/1864-335/ a000194 Unkelbach, C. (2015). Looking back and looking forward.

Social Psychology, 46, 1–3. doi: 10.1027/1864-335/a000237 Wesselmann, E. D., Williams, K. D., Pryor, J. B., Eichler, F. A., Gill, D. M., & Hogue, J. D. (2014). Revisiting Schachter’s research on rejection, deviance, and communication (1951).

Social Psychology, 45, 164–169. doi: 10.1027/1864-335/ a000180 Westfall, J., Kenny, D. A., & Judd, C. M. (2014). Statistical power and optimal design in experiments in which samples of participants respond to samples of stimuli. Journal of Experimental Psychology: General, 143, 2020–2045.

Westfall, J., Judd, C. M., & Kenny, D. A. (2015). Replicating studies in which samples of participants respond to samples of stimuli. Perspectives on Psychological Science, 10, 390–399.

Christian Unkelbach Department of Psychology Universität zu Köln Richard-Strauss-Str. 2 50931 Köln Germany Tel. +49 221 470-2001 E-mail christian.unkelbach@uni-koeln.de

Social Psychology 2016; Vol. 47(1):1–3

Original Article

The Effects of Invoking Stereotype Excuses on Perceivers’ Character Trait Inferences and Performance Attributions Jade S. Jenkins1 and John J. Skowronski2 1

Texas A&M University, Texarkana, TX, USA, 2Northern Illinois University, DeKalb, IL, USA

Abstract. This investigation examined perceivers’ character trait inferences and performance attributions in response to a target who invoked a gender stereotype to excuse poor math performance. Furthermore, this investigation sought to compare the effects of this excuse to the effects tproduced by a non-stereotype excuses and the mere mention of a stereotype. Results revealed that invoking a gender stereotype excuse for poor math performance may elicit especially negative effects on perceptions of an excuse-maker’s: (a) overall character; (b) effectualness; (c) responsibility for the performance outcome; and (d) control over the performance outcome.

Keywords: stereotypes, impression formation, impression management, excuses

Stigmatized targets may sometimes cite performance stereotypes (e.g., ‘‘Women are bad at math’’) to excuse their poor performances (Burkley & Blanton, 2009; Goffman, 1963; Jones, 1979), especially when success on stereotype-relevant tasks is perceived as difficult to achieve (Kim, Lee, & Hong, 2012). Stereotype excuses may be used to protect the self against threats (Burkley & Blanton, 2008), to fulfill assimilation and differentiation needs (Turner, Hogg, Oakes, Reicher, & Wetherell, 1987), to rationalize the status quo (Bell & Burkley, 2014), and to relieve awkward social interactions (Ryan, BiemanCopland, See, Ellis, & Anas, 2002). However, reliance on stereotype excuses can decrease performance motivation on future tasks (Tyler & Feldman, 2007), reduce efforts to create social change (Laurin, Kay, & Shepherd, 2011), and may elicit negative affective reactions (Burkley, Andrade, Stermer, & Bell, 2013) from others. Hence, stereotype excuses can be a ‘‘double-edged sword’’ for the stigmatized targets that invoke them (Burkley & Blanton 2009).

The primary goal of excuse-making is to minimize the consequences of negative outcomes (Schlenker, Pontari, & Christopher, 2001). In pursuit of this goal, excuses sometimes backfire and cause excuse-makers to be evaluated negatively by perceivers (Pontari, Schlenker, & Christopher, 2002). Stereotype excuses would likely elicit evaluations that are more negative than those elicited by non-stereotype excuses or the mention of a stereotype. Indeed, invoking a stereotype excuse not only implicates the excuse-maker; the excuse-maker’s ingroup has also been implicated Social Psychology 2016; Vol. 47(1):4–14 DOI: 10.1027/1864-9335/a000253

(Bell & Burkley, 2014). Furthermore, citing a stereotype as an excuse would be seen as inconsistent with social norms (Allport, 1954; Devine, 1989; Fiske, Cuddy, Glick, & Xu, 2002). Despite these ideas, neither the excuse-making literature nor the emerging literature on stereotype excuses has examined the effects that stereotype excuses may have on perceptions central to the evaluation of excuse-makers.

In this investigation, we examine perceivers’ evaluations of women who invoke a gender stereotypes for excuse their poor math performance. The first goal was to examine the effects of this gender stereotype excuse on: (a) perceptions of the excuse-maker’s character traits; and (b) attributions about the excuse-maker’s poor performance. Our second goal was to examine competing explanations for the locus of these effects.

Stereotype Excuses and Character Trait Perceptions According to the character trait framework of excusemaking (Pontari et al., 2002; Schlenker et al., 2001; Tyler & Feldman, 2007), three conditions determine the effectiveness of excuses.

First, excuses must be seen as credible (or the target may be seen as deceitful). Dialog concerning women’s math underperformance has increasingly acknowledged the role of factors not intrinsic to gender (e.g., stereotype threat; 2016 Hogrefe Publishing

J. S. Jenkins & J. J. Skowronski: The Effects of Invoking

Spencer, Steele, & Quinn, 1999). Therefore, the women/ math stereotype excuse could be perceived as misleading and may motivate some perceivers to counterargue or react against these claims (e.g., Kray, Reb, Galinsky, & Thompson, 2004). When this clash occurs, perceivers will question an excuse-maker’s sincerity (Schlenker et al., 2001). Second, excuses should balance short-term disengagement from the current failure with the promise of future corrective action (or the target will be seen as low in effectualness). Gender stereotype excuses are incorporated excuses (Snyder & Higgins, 1988), in that they highlight an ongoing characteristic of the excuse-maker (his or her gender group). If a gender stereotype excuse is being cited as a cause for poor math performance, perceivers may suspect that poor performance will persist. Thus, perceivers would likely rate her as low in effectualness (see Ryan et al., 2002). Finally, excuses must suggest goodwill toward others (or the target will be perceived as selfabsorbed). A woman who invokes a gender stereotype to excuse poor math performance could be perceived as a ‘‘troublemaker’’ or ‘‘complainer’’ (Kaiser & Miller, 2001, 2003). Moreover, by highlighting harmful information in the form of an excuse, she would also violate the female gender role prescription of directing politeness and warmth toward others (Prentice & Carranza, 2002). When excuses are viewed as hostile or narcissistic, excuse-makers will be seen as self-absorbed (Pontari et al., 2002).

Stereotype Excuses and Performance Attributions Ideas about performance attributions (e.g., Weiner, 2005) and work that links attributions to excuses (e.g., Schlenker, Britt, Pennington, Murphy, & Doherty, 1994) prompted exploration of three performance attributions that might be affected by the use of a gender stereotype to excuse poor math performance.

First, perceivers may view a woman who invokes the women/math excuse as attempting to avoid personal responsibility (Schlenker et al., 1994). Given that developmental opportunities in math have become increasingly accessible (e.g., Draugalis, Plaza, Taylor, & Meyer, 2014), perceivers may become upset with the excuse-maker for refusing to take personal responsibility for her poor math performance (Bell & Burkley, 2014). Thus, a woman who cites a stereotype to excuse poor math performance would likely be perceived as highly responsible for her poor math performance. Second, many perceivers may think that people can acquire math skills through sufficient effort (Good, Rattan, & Dweck, 2012). Perceivers may attribute women’s math success to high effort and believe that high effort is a more necessary component for women’s math success than it is for men’s math success (Parsons, Meece, Adler, & Kaczala, 1982; Yee & Eccles, 1988). Thus, in the face of these beliefs, many perceivers may perceive that a gender stereotype excuse for poor math performance has been invoked to mask low personal effort. Finally, perceptions of controllability over performance outcomes are high when information about a task’s characteristics, the excuse 2016 Hogrefe Publishing

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maker’s capabilities, and available resources suggest it is possible for the excuse-maker to succeed (Schlenker et al., 2001). Perceivers may feel that there is nothing unusual about the demands associated with a math task, especially in light of preparation time, available practice activities, and other tools available to bring about volitional change. Thus, despite poor performance, perceivers would likely view a woman who invokes a gender stereotype excuse for poor math performance as having had high control over the performance outcome.

Study 1 In a Pilot Study, judgments made about a woman who invoked a gender stereotype to excuse poor math performance were compared to those made when she eschewed excuses for her performance. For details on the Pilot Study, please review Electronic Supplementary Material 1. Results suggested that perceivers made negative character trait judgments about her when she invoked the gender stereotype excuse. However, the gender stereotype excuse did not influence performance attributions. This Pilot Study design could not be used to determine the locus of these effects.

In Study 1, we modified the method developed in the Pilot Study to examine the locus of gender stereotype excuse effects. This examination compared two competing possibilities. One possibility is that additive effects could emerge, such that: (1) the act of excuse-making might have negative effects on target judgments; (2) activating the women/math stereotype might have negative effects on target judgments; and (3) when these two manipulations are used simultaneously, their effects on target judgments are simply additive (i.e., exposure to both manipulations causes more negative judgments than exposure to any single manipulation).

A second possibility is that the effects of these two variables are interactive. This may occur, for example, if exposure to the women/math stereotype by itself does not have negative consequences for actor perceptions, but that using the stereotype in the context of an excuse does produce such consequences. In either case, if stereotype excuses do contribute to the interpersonal perception consequences of excuse-making, we would expect analyses to yield evidence (either via interactions or main effects) that invoking the women/math stereotype in an excuse had effects on judgments of excuse-making targets that go beyond the effects produced by the mere act of excuse-making or mentioning a stereotype.

Method Participants Two hundred forty participants from the United States were recruited via a survey link posted on Amazon’s Mechanical Turk (MTurk; see Behrend, Sharek, Meade, & Wiebe, 2011; Social Psychology 2016; Vol. 47(1):4–14

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J. S. Jenkins & J. J. Skowronski: The Effects of Invoking

Table 1. Study 1: Means, standard deviations, reliabilities, and correlations among character trait indices and performance attribution indices Variable name 1.

2.

3.

4.

5.

6.

7.

Overall character Deceitfulness Effectualness Self-absorption Responsibility Effort Controllability

M

SD

3.89 1.64 3.75 1.51 3.35 3.33 3.64

1.18 1.02 1.05 1.36 1.00 1.32 1.13

1 .89 .75** .84** .46** .11 .54** .03

2

3

.82 .70** .65** .03 .49** .03

.90 .37** .04 .63** .01

4

.92 .07 .36** .01

5

6

7

.81 .01 .54**

.94 .02

.90

Notes. Reliabilities located along diagonal in bold. **p < .01.

Buhrmester, Kwang, & Gosling, 2011). Of the 240 participants who initially accessed the survey link, 228 completed the entire study. All participants were compensated with US$0.25.

Given data quality concerns with online studies (Meade & Craig, 2012), three instructed response items were inserted in randomly-selected locations within the study.

Each item instructed participants to select a specific response option (e.g., ‘‘Please select ‘Strongly Agree’ for this item.’’). Ten participants did not respond correctly to one or more of these three items; their responses were excluded prior to analyses. Thus, the final sample contained 218 participants (58.7% women, 77.1% Caucasian) with a mean age of 33.06 years (SD = 10.57).

Procedures Participants read an article describing a fictitious university’s decision to offer GRE tutoring to students. In this article, a student worker for the university testing center was interviewed about the need for tutoring on campus. During the interview, the student discussed her recent poor performance on the quantitative portion of a practice GRE test.

Participants were randomly assigned to one of four conditions. Participants randomly assigned to the no excuse condition read an excerpt in which the target explains: ‘‘I got a poor score. Still, it was good to at least find out where I stood. . ..’’

Participants assigned to the stereotype excuse condition read a version of the article in which the student invoked a gender stereotype excuse to explain her poor performance: ‘‘I got a poor score, but I think everyone knows that women are just worse at figuring out these kinds of questions, though—math is harder for us and we are much better at verbal stuff, and I think that explains my math score. Still, it was good to at least find out where I stood. . ..’’

1

In the non-stereotype excuse condition, the student cited a general group-based explanation (her major) for her performance, explaining: ‘‘I got a poor score, but I think everyone in my major is just worse at figuring out these kinds of questions, though—math is harder for us and we are much better at verbal stuff, and I think that explains my math score. Still, it was good to at least find out where I stood. . ..’’

Finally, in the stereotype activation condition, the gender stereotype was not raised by the target. Instead, information pertaining to beliefs about women’s math abilities was inserted into the article author’s discussion, explaining: ‘‘Indeed, as many people are already aware, research has frequently shown that women under perform in comparison to men in mathematics. However, women also outperform men on verbal tests.’’

After reading the article, participants completed a questionnaire in which they made judgments about the student.

Measures Participants provided judgments about the target’s character traits and reported performance attributions. Prior to averaging the responses that comprised each index, responses were reverse-coded as needed.

Means, standard deviations, reliabilities, and correlations among all character trait indices and performance attribution indices appear in Table 1.1 Character Trait Indices Participants viewed trait words associated with four character trait indices (taken from Pontari et al., 2002): (1) overall character (3 items); (2) deceitfulness (4 items); (3) effectualness (6 items); and (4) self-absorption (6 items).

Reliabilities reported in this article are based on our datasets.

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Table 2. Study 1: Means, standard deviations, analysis of variance (ANOVA) F-values, and effect size results for character trait indices as a function of excuse conditions and stereotype conditions Stereotype

No stereotype

M

SD

M

SD

M

SD

3.25 4.14 3.67

1.37 1.04 1.30

3.94 4.31 4.12

0.99 1.00 1.01

3.58 4.23 3.89

1.24 1.02 1.18

2.10 1.53 1.83

1.06 1.00 1.06

1.48 1.37 1.43

0.85 0.99 0.92

1.80 1.45 1.64

1.01 0.99 1.02

3.28 4.00 3.63

1.07 0.94 1.07

3.73 4.05 3.89

1.06 0.97 1.03

3.50 4.03 3.75

1.08 0.95 1.05

2.08 1.26 1.70

1.56 1.15 1.44

1.39 1.23 1.31

1.22 1.29 1.25

1.75 1.24 1.51

1.44 1.22 1.36

Dependent variable Overall character Excuse No excuse Total Deceitfulnessb Excuse No excuse Total Effectualnessc Excuse No excuse Total Self-absorptiond Excuse No excuse Total

Total

Effect size (g2p)

ANOVA F

a

E

S

E·S

E

S

E·S

17.41***

8.14**

2.87

.08

.04

.01

6.31*

8.42**

2.90

.03

.04

.01

14.61***

3.27

2.06

.06

.02

.01

7.30**

3.97*

3.15

.03

.02

.02

Notes. E = excuse main effect; S = stereotype main effect; E · S = Excuse · Stereotype interaction. adf = 214. bdf = 210. cdf = 212. d df = 209. Degrees of freedom vary due to occasional missing data. *p < .05. **p < .01. ***p < .001.

In response to each trait word, participants indicated the extent to which they agreed on a 0 (= strongly disagree) to 6 (= strongly agree) scale that each word was characteristic of the student from the article.

excuse condition and: (1) the no excuse condition; (2) the stereotype activation condition; and (3) the non-stereotype excuse condition.

Means, standard deviations, F-values, and effect sizes pertaining to the character trait indices and performance attribution indices appear in Tables 2 and 3.

Performance Attribution Indices Participants responded to 12 items (4 items each) assessing their perceptions of the student’s: (1) responsibility2 for poor performance; (2) effort expended during the task; and (3) degree of controllability she was perceived to have had over her performance. Ratings were made using a 0 (i.e., not very _____) to 5 (i.e., very _____) scale. For example, one item asked ‘‘How responsible do you consider [the target] to be for her performance outcome?’’ Responses to this item were made on a 0 (= not very responsible) to 5 (= very responsible) scale.

Results Each index was separately subjected to a 2 (Excuse: excuse, no excuse) · 2 (Stereotype: stereotype, no stereotype) ANOVA. Only significant results are described. Significant interactions were decomposed via planned comparisons examining differences in judgments between the stereotype 2

Character Traits An excuse main effect for the overall character index, F(1, 214) = 17.41, p < .001, g2p = .08, revealed that the target was perceived to have a less favorable character when she invoked an excuse (M = 3.58, SD = 1.24) than when she did not (M = 4.23, SD = 1.02). A stereotype main effect F(1, 214) = 8.14, p = .005, g2p = .04, revealed that the target was perceived to have a less favorable character when a stereotype had been mentioned (M = 3.67, SD = 1.30) than when no stereotype was mentioned (M = 4.12, SD = 1.01).

Results also revealed an excuse main effect for deceitfulness, F(1, 210) = 6.31, p = .013, g2p = .03, suggesting that the target was viewed as more deceitful when she invoked an excuse (M = 1.80, SD = 1.01) than when she did not (M = 1.45, SD = 0.99). Results also revealed a significant stereotype main effect, F(1, 210) = 8.42, p = .004, g2p = .04. The target was viewed as more deceitful when a

Readers who have read about the Pilot Study in the supplementary materials should note one modification made to the responsibility index items for Study 1 and Study 2. The responsibility index demonstrated poor reliability in the Pilot Study, so the poor-performing items were rewritten. The new responsibility index consisted of items assessing how responsible [the target] was for her performance outcome, how much [the target] could be blamed for her performance outcome, how much influence [the target] had over her performance outcome, and how in charge [the target] was over her performance outcome. These changes greatly improved the reliability of the responsibility index (a = .81).

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Table 3. Study 1: Means, standard deviations, analysis of variance (ANOVA) F-values, and effect size results for performance attribution indices as a function of excuse conditions and stereotype conditions

Dependent variable

Stereotype

No stereotype

M

SD

M

SD

M

SD

3.57 3.22 3.40

1.00 1.03 1.02

3.24 3.35 3.29

0.94 1.02 0.98

3.41 3.28 3.35

0.98 1.02 1.00

2.91 3.48 3.18

1.30 1.28 1.32

3.27 3.74 3.50

1.37 1.19 1.30

3.08 3.61 3.33

1.34 1.24 1.32

4.00 3.31 3.67

0.98 1.02 1.06

3.65 3.57 3.61

1.09 1.33 1.21

3.83 3.44 3.64

1.04 1.19 1.13

Total

S

E·S

E

S

E·S

0.79

0.51

2.90

.00

.00

.01

8.93**

3.15

0.09

.04

.01

.00

6.60*

0.09

4.26*

.03

.00

.02

E

a

Responsibility Excuse No excuse Total Efforta Excuse No excuse Total Controllabilitya Excuse No excuse Total

Effect size (g2p)

ANOVA F

Note. E = excuse main effect; S = stereotype main effect; E · S = Excuse · Stereotype interaction. adf = 214. *p < .05. **p < .01.

Performance Attributions No significant effects emerged when predicting perceivers’ attributions of responsibility for the target’s performance.

Furthermore, only a significant excuse main effect emerged for attributions of effort, F(1, 214) = 8.93, p = .003, g2p = .04. Participants perceived that the target expended less performance effort when she invoked an excuse (M = 3.08, SD = 1.34) than when she did not (M = 3.61, SD = 1.24). Finally, results revealed a significant excuse main effect for controllability attributions, F(1, 214) = 6.60, p = .003, g2p = .03. Participants rated the target as having more control over the performance outcome when she invoked an excuse (M = 3.83, SD = 1.04) than when she did not (M = 3.44, SD = 1.19).

A significant Excuse · Stereotype interaction also emerged (see Figure 1) when predicting controllability attributions,

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6 5 Controllability

stereotype had been mentioned (M = 1.83, SD = 1.06) than when no stereotype had been mentioned (M = 1.43, SD = 0.92).

The effectualness results yielded only a significant excuse main effect, F(1, 212) = 14.61, p < .001, g2p = .06.

The target was perceived as less effectual when she invoked an excuse (M = 3.50, SD = 1.08) than when she did not (M = 4.03, SD = 0.95).

Finally, the self-absorption results revealed a significant excuse main effect, F(1, 209) = 7.30, p = .007, g2p = .03.

The target was perceived as more self-absorbed when she invoked an excuse for her performance (M = 1.75, SD = 1.44) than when she did not (M = 1.24, SD = 1.22).

Results also revealed a significant stereotype main effect, F(1, 209) = 3.97, p = .048, g2p = .02, suggesting that the target was seen as more self-absorbed when a stereotype had been mentioned (M = 1.70, SD = 1.44) than when no stereotype had been mentioned (M = 1.31, SD = 1.25).

4 3 2 1 0

Stereotype Excuse

No Stereotype No Excuse

Figure 1. Study 1 excuse condition by stereotype condition interaction predicting attributions of controllability over the performance outcome. The stereotype activation condition corresponds to the stereotype/no excuse data.

Furthermore, the control condition corresponds to the no stereotype/no excuse data. Error bars indicate ±1 standard error of the mean.

F(1, 214) = 4.26, p = .040, g2p = .02. In comparison to controllability attributions in the stereotype excuse condition, the target was rated as having significantly less control over the performance outcome in: (a) the no excuse condition, t(214) = 2.05, p = .042; and (b) the stereotype activation condition, t(214) = 3.32, p = .001.

Study 2 The data from Study 1 suggest that use of a gender stereotype in an excuse for poor math performance worsens the 2016 Hogrefe Publishing

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Table 4. Study 2: Means, standard deviations, reliabilities, and correlations among character trait indices and performance attribution indices Variable name 1.

2.

3.

4.

5.

6.

7.

Overall character Deceitfulness Effectualness Self-absorption Responsibility Effort Controllability

M

SD

3.54 2.00 3.47 1.82 3.22 2.82 3.48

1.05 0.99 1.04 1.40 1.06 1.34 1.30

1 .86 .72** .80** .41** .22** .55** .12

2

3

.80 .65** .62** .13 .58** .05

.91 .31** .23** .66** .07

4

5

.93 .10 .42** .05

.83 .06 .58**

6

7

.96 .05

.93

Notes. Reliabilities located along diagonal in bold. *p < .05. **p < .01.

interpersonal perception consequences of excuse-making.

These effects were largely additive, and not interactive, such that the negative effects of mentioning the stereotype in the story were simply added to the negative effects of excuse-making. The only significant interaction between excuse-making and activating the stereotype that emerged did so when predicting controllability attributions: Mentioning the gender stereotype did not affect perceptions of outcome controllability when the idea was not used as an excuse, but did heighten perceptions of outcome controllability when the idea was used as an excuse.

However, some might claim that these data are weaker than they appear because of two confounds identified in the study design. First, the stereotype information mentioned in the stereotype activation condition featured performance stereotypes about both men and women; the stereotype excuse only highlighted a performance stereotype about women. Second, the stereotype information in the stereotype activation condition was introduced by a third party (the author of the article that participants read).

In comparison, in the stereotype excuse condition, the stereotype was raised by the target. Thus, in Study 1, it is unclear whether the effects of the excuse manipulation in the stereotype activation condition were actually caused by the excuse manipulation, or were caused by different sources or the different stereotype information conveyed in the two conditions.

Accordingly, in Study 2, a minor modification was made to the story that participants read in the gender stereotype activation condition. In this condition, the target (rather than the author of the article) introduces the stereotype about women only, but did not invoke this information as an excuse for poor performance.

Method Participants Two hundred sixty participants from the United States accessed the online study link through MTurk. Of these participants, 241 completed the study. Furthermore, 13 participants failed to correctly respond to one or more instructed response items (described in Study 1). Thus, the final 2016 Hogrefe Publishing

sample contained 228 participants (56.6% women, 78.5% Caucasian); the mean age was 32.80 years (SD = 10.80).

Procedure Each participant was randomly assigned to one of four conditions. The materials for the no excuse condition, nonstereotype excuse condition, and stereotype excuse condition duplicated those used in Study 1. However, in the stereotype activation condition, the materials were revised so that the stereotype information was introduced by the target: ‘‘I got a poor score. Everyone says that women are just worse at figuring out these kinds of questions—that math is harder for us and we are much better at verbal stuff—but I don’t think that explains my math score. Still, it was good to at least find out where I stood. . ..’’

After participants finished reading the article, they provided responses to the same character trait items and performance attribution items used in Study 1. Means, standard deviations, correlations, and reliabilities among all character indices and performance attributions indices appear in Table 4.

Results As in Study 1, each character trait index and performance attribution index was subjected to a 2 (Excuse: excuse, no excuse) · 2 (Stereotype: stereotype, no stereotype) ANOVA. Only significant results are noted. Interaction decompositions proceeded as described in Study 1. Means, standard deviations, F-values, and effect sizes for all indices appear in Tables 5 and 6.

Character Traits Results for the overall character index yielded a significant excuse main effect, F(1, 222) = 10.20, p = .001, g2p = .05, Social Psychology 2016; Vol. 47(1):4–14

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Table 5. Study 2: Means, standard deviations, analysis of variance (ANOVA) F-values, and effect size results for character trait indices as a function of excuse conditions and stereotype conditions.

Dependent variable Overall character Excuse No excuse Total Deceitfulnessb Excuse No excuse Total Effectualnessc Excuse No excuse Total Self-absorptionb excuse No excuse Total

Stereotype

No stereotype

M

SD

M

SD

M

SD

2.92 3.67 3.28

1.16 1.09 1.18

3.73 3.84 3.78

0.84 0.85 0.84

3.33 3.75 3.54

1.08 0.97 1.05

2.33 1.85 2.10

1.07 1.01 1.06

1.95 1.87 1.91

0.86 0.98 0.92

2.14 1.86 2.00

0.98 0.99 0.99

2.93 3.61 3.27

1.14 1.08 1.15

3.68 3.66 3.67

0.90 0.87 0.88

3.31 3.64 3.47

1.09 0.97 1.04

2.35 1.78 2.07

1.48 1.46 1.49

1.73 1.46 1.60

1.33 1.22 1.28

2.03 1.62 1.83

1.43 1.34 1.40

Total

Effect size (g2p)

ANOVA F

a

E

S

E·S

E

S

E·S

10.20**

13.71***

6.01*

.05

.06

.03

4.80*

1.89

2.33

.02

.01

.01

6.12*

8.98**

7.01*

.03

.04

.03

5.33*

6.51*

0.68

.02

.03

.00

Notes. E = excuse main effect; S = stereotype main effect; E · S = Excuse · Stereotype interaction. adf = 222. bdf = 219. cdf = 221.

Degrees of freedom vary due to occasional missing data. *p < .05. **p < .01. ***p < .001.

Table 6. Study 2: Means, standard deviations, analysis of variance (ANOVA) F-values, and effect size results for performance attribution indices as a function of excuse conditions and stereotype conditions

Dependent variable

Stereotype

No stereotype

M

SD

M

SD

M

SD

3.59 3.03 3.32

1.15 1.05 1.13

3.13 3.13 3.13

0.82 1.13 0.99

3.36 3.08 3.22

1.02 1.09 1.06

2.28 2.96 2.61

1.40 1.35 1.42

2.97 3.05 3.01

1.24 1.26 1.25

2.63 3.01 2.82

1.36 1.30 1.34

4.04 3.20 3.63

1.37 1.32 1.41

3.31 3.35 3.33

1.15 1.22 1.18

3.67 3.28 3.48

1.31 1.27 1.30

Total

a

Responsibility Excuse No excuse Total Efforta Excuse No excuse Total Controllabilitya Excuse No excuse Total

Effect size (g2p)

ANOVA F E

S

E·S

E

S

E·S

4.09*

1.78

4.09*

.02

.01

.02

4.76*

5.16*

3.01

.02

.02

.01

5.64*

3.07

6.88**

.03

.00

.03

Note. E = excuse main effect; S = stereotype main effect; E · S = Excuse · Stereotype interaction. adf = 224. *p < .05. **p < .01. ***p < .001.

and a significant stereotype main effect, F(1, 222) = 13.71, p < .001, g2p = .06. These were qualified by a significant Excuse · Stereotype interaction, F(1, 222) = 6.01, p = .015, g2p = .03 (see Figure 2). In comparison to ratings in the stereotype excuse condition, the target was rated as having significantly more favorable character in the: (a) no excuse condition, t(222) = 4.95, p < .001; (b) stereotype activation condition, t(222) = 3.96, p < .001; and (c) nonstereotype excuse condition, t(222) = 4.44, p < .001.

The results for the deceitfulness index only revealed that the target was perceived as more deceitful when she Social Psychology 2016; Vol. 47(1):4–14

invoked an excuse (M = 2.14, SD = 0.98) than when she did not (M = 1.86, SD = 0.99), F(1, 219) = 4.80, p = .029, g2p = .02.

Results for the effectualness index revealed a significant excuse main effect, F(1, 221) = 6.12, p = .014, g2p = .03, and a significant stereotype main effect, F(1, 221) = 8.98, p = .003, g2p = .04. These were qualified by a significant Excuse · Stereotype interaction, F(1, 221) = 7.01, p = .009, g2p = .03 (see Figure 3). In comparison to the ratings in the stereotype excuse condition, the target was perceived as significantly more effectual in the: (a) no excuse 2016 Hogrefe Publishing

6

6

5

5

4

Responsibility

Overall Character

J. S. Jenkins & J. J. Skowronski: The Effects of Invoking

3 2 1 0

11

4 3 2 1

Stereotype Excuse

No Stereotype No Excuse

Figure 2. Study 2 excuse condition by stereotype condition interaction predicting overall character perceptions.

The stereotype activation condition corresponds to the stereotype/no excuse data. Furthermore, the control condition corresponds to the no stereotype/no excuse data. Error bars indicate ±1 standard error of the mean.

0

Stereotype

No Stereotype

Excuse

No Excuse

Figure 4. Study 2 excuse condition by stereotype condition interaction predicting attributions of responsibility for performance outcome. The stereotype activation condition corresponds to the stereotype/no excuse data.

Furthermore, the control condition corresponds to the no stereotype/no excuse data. Error bars indicate ±1 standard error of the mean.

6

Performance Attributions

Effectualness

5 4 3 2 1 0

Stereotype Excuse

No Stereotype No Excuse

Figure 3. Study 2 excuse condition by stereotype condition interaction predicting effectualness perceptions. The stereotype activation condition corresponds to the stereotype/no excuse data. Furthermore, the control condition corresponds to the no stereotype/no excuse data. Error bars indicate ±1 standard error of the mean.

condition, t(221) = 3.88, p < .001; (b) stereotype activation condition, t(221) = 3.58, p < .001; and (c) non-stereotype excuse condition, t(222) = 4.02, p < .001.

Finally, results for the self-absorption index revealed that: (1) the target was perceived to be more self-absorbed when she invoked an excuse (M = 2.03, SD = 1.43) than when she did not (M = 1.62, SD = 1.34), F(1, 219) = 5.33, p = .022, g2p = .02, and (2) the target was perceived to be more self-absorbed when the gender stereotype had been mentioned (M = 2.07, SD = 1.49) than when it had not been mentioned (M = 1.60, SD = 1.28), F(1, 219) = 6.51, p = .011, g2p = .03.

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On the index assessing responsibility for the performance outcome, the target was perceived to be more responsible when she invoked an excuse (M = 3.36, SD = 1.02) than when she did not (M = 3.08, SD = 1.09), F(1, 224) = 4.09, p = .044, g2p = .02. A significant Excuse · Stereotype interaction also emerged on this index, F(1, 224) = 4.09, p = .044, g2p = .02 (see Figure 4).

In comparison to responsibility attributions in the stereotype excuse condition, participants attributed less responsibility to the target in the: (a) no excuse condition, t(224) = 2.37, p = .018; (b) stereotype activation condition, t(224) = 2.83, p = .005; and (c) non-stereotype excuse condition, t(224) = 2.39, p = .017.

On the index assessing perceptions of performance effort, the target was perceived as having expended less performance effort when she invoked an excuse (M = 2.63, SD = 1.36) than when she did not (M = 3.01, SD = 1.30), F(1, 224) = 4.76, p = .030, g2p = .02. Results for this index also showed that the target was perceived as having expended less performance effort when the gender stereotype was mentioned (M = 2.61, SD = 1.42) than when it was not (M = 3.01, SD = 1.25), F(1, 224) = 5.16, p = .024, g2p = .02. Finally, on the index assessing attributions of controllability over the performance outcome, the target was perceived as having more control over her performance outcome when she invoked an excuse (M = 3.67, SD = 1.31) than when she did not (M = 3.28, SD = 1.27), F(1, 224) = 5.64, p = .018, g2p = .03. A significant Excuse · Stereotype interaction also emerged on the controllability index, F(1, 224) = 6.88, p = .009, g2p = .03 (see Figure 5). In comparison to ratings in the stereotype excuse condition, the target was rated as having significantly less control over the performance outcome Social Psychology 2016; Vol. 47(1):4–14

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Controllability

5 4 3 2 1 0

Stereotype Excuse

No Stereotype No Excuse

Figure 5. Study 2 excuse condition by stereotype condition interaction predicting attributions of controllability over the performance outcome. The stereotype activation condition corresponds to the stereotype/no excuse data.

Furthermore, the control condition corresponds to the no stereotype/no excuse data. Error bars indicate ±1 standard error of the mean. in the: (a) no excuse condition, t(224) = 2.92, p = .004; (b) stereotype activation condition, t(224) = 3.50, p = .001; and (c) non-stereotype excuse condition, t(224) = 3.12, p < .002.

General Discussion Characteristics of excuses predict specific character traitbased evaluations of excuse-makers (Pontari et al., 2002).

This investigation contributes to both the general excusemaking literature and the emerging stereotype excuse literature by demonstrating the effects of a gender stereotype excuse (and the locus of these effects) on perceivers’ character trait inferences and performance attributions. Our results suggested that sometimes the negative effects of using the women/math stereotype as an excuse could be accounted for by simply adding the negative effects of excuse-making and mentioning a stereotype together. However, sometimes the effects of the women/math stereotype emerged in interactions – which typically showed that mentioning the women/math stereotype by itself did not have negative consequences for actor perceptions, but that using the stereotype in the context of an excuse did produce such consequences.

The gender stereotype excuse-making target was evaluated as having especially unfavorable character and as being low in effectualness. Excuse-makers who are viewed in these ways signal to perceivers that future poor performance is likely and that perceivers may have reason to question how reliable the excuse-maker may be in the future (Schlenker et al., 2001). Thus, women who invoke a gender stereotype to excuse poor math performance are perceived

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as chronic underperformers. Future research could explore the boundary conditions in which perceptions of a gender stereotype excuse-makers’ effectualness may not be questioned. For example, according to Schlenker et al.’s (2001) character trait framework, it is possible that negative evaluations could be tempered if the gender stereotype excuse-making target (a) emphasizes why alleged deficiencies in her gender group’s performance have been influenced by factors outside of her group’s control, but (b) reveals plans to take corrective action to overcome these hindrances.

Use of the gender stereotype as an excuse for poor math performance also affects how people think about the causes of the excuse-maker’s poor math performance. When the target used the gender stereotype as an excuse, perceivers viewed the excuse-maker as especially responsible for, and in control of, her performance outcome. Targets who are perceived in these ways tend to be blamed by others for negative outcomes, are perceived as being at fault for those negative outcomes, and are perceived as undeserving of receiving help or sympathy from others (Feather, 2006).

It is possible that perceivers could have been counterarguing the excuse by invoking beliefs that performance is changeable. Hence, one possible direction for future research is to assess the thoughts (e.g., via a listed thoughts protocol) that people have in response to a target’s use of the women/math excuse. Another direction might explore whether effects that emerged in our studies are moderated by a perceiver’s implicit beliefs (e.g., Dweck, Chiu, & Hong, 1995). Entity theorists (e.g., who believe that traits are fixed) may not react against the use of the women/math stereotype in the way that one might expect from incremental theorists (who believe that traits are malleable). A similar approach might explore possible moderation of the results that we report by the extent to which people believe the gender stereotype. People who believe the gender stereotype may see its use as perfectly reasonable (and not counterargue) compared to those who do not believe the stereotype.

Future research should also determine the extent to which stereotype excuses based on other stereotypes replicate or diverge from perceptions elicited in response to a women/math stereotype excuse. For example, the relationship between age and memory failure is strongly endorsed in Western culture (e.g., Erber & Prager, 2000). Perceivers may be inclined to believe an elderly person who cites an age stereotype to excuse memory failure. If this is true, the Schlenker et al. (2001) excuse framework would predict that perceivers may not judge the character of an age/memory excuse-maker to be as negative as the character of a woman/math excuse-maker.

Possible Limitations Although the use of written stimuli is consistent with methodology used in past excuse studies (e.g., Pontari et al., 2002), some might claim that results might differ if behaviors were directly observed. However, research using direct

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observations of behavior, even brief ones (Ambady & Rosenthal, 1992), suggests that this is unlikely. In fact, because of the focus on the excuse-maker in such direct observation studies, reactions to direct observation in such studies may even be extremitized relative to reactions derived from text.

The exact nature of the information presented in our studies should also be considered when interpreting our findings. For example, when making her excuse, our target cites both a negative stereotype (women are bad at math) and a positive stereotype (women are good at verbal tasks).

It is possible that perceivers’ evaluations of the excusemaker may have been different if the positive stereotype had not been included. We assume that participants recognized that the target was trying to make an excuse for her poor math performance, and that the women/verbal skills stereotype merely served as a context for the women/math excuse. The negativity of the evaluations observed in this investigation is also similar to patterns observed in related research (e.g., Burkley et al., 2013). Nonetheless, it is possible that any single detail of any research design might cause a specific outcome to occur. Therefore, echoing Schmidt (2009), we strongly advocate replication and extension of these studies using methods and measures that differ from the ones that we employed. Strong conclusions about effects in this domain will only be possible after a substantial number of such studies have been conducted and their findings assessed and integrated (e.g., via metaanalysis).

An additional potential limitation is that our investigation focused on retrospective stereotype excuse-making (invoking the excuse after a negative performance outcome). We did not examine circumstances in which stereotype excuses are invoked prior to a performance (Erber & Prager, 2000). Thus, readers should be cautious in generalizing our findings, and their implications, to such circumstances.

Conclusions Relative to other excuses, excuses that contain the women/ math stereotype appear to be especially likely to undermine perceptions of an excuse-maker’s overall character, effectualness, responsibility for the performance outcome, and perceived control over the performance outcome. Thus, excuse-makers who invoke stereotype excuses must weigh the potential intrapersonal benefits of stereotype excusemaking with the impression management consequences associated with this excuse-making strategy.

Acknowledgments This article was derived from a Master’s Thesis conducted by the first author under supervision of the second. We thank the Master’s committee members, Amanda Durik and Lisa Finkelstein, for their suggestions during the thesis process.

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Electronic Supplementary Material The electronic supplementary material is available with the online version of the article at http://dx.doi.org/10.1027/ 1864-9335/a000253 ESM 1. Word file (SP Pilot Study Supplement.docx).

This Word file contains detailed information on the hypotheses, methodology, and results from the Pilot Study.

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Good, C., Rattan, A., & Dweck, C. S. (2012). Why do women opt out? Sense of belonging and women’s representation in mathematics. Journal of Personality and Social Psychology, 102, 700–717. doi: 10.1037/a0026659 Jones, E. E. (1979). The rocky road from acts to disposition.

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Excuses and character: Identifying the problematic aspects of excuses. Journal of Social and Clinical Psychology, 21, 497–516. doi: 10.1521/jscp.21.5.497.22621 Prentice, D. A., & Carranza, E. (2002). What women and men should be, shouldn’t be, are allowed to be, and don’t have to be: The contents of prescriptive gender stereotypes. Psychology of Women Quarterly, 26, 269–281. doi: 10.1111/ 1471-6402.t01-1-00066 Ryan, E. B., Bieman-Copland, S., See, S. T. K., Ellis, C. H., & Anas, A. P. (2002). Age excuses: Conversational management of memory failures in older adults. The Journals of Gerontology: Psychological Sciences, 57, P256–P267.

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Psychological Review, 101, 632–652. doi: 10.1037/0033295X.101.4.632 Schlenker, B. R., Pontari, B. A., & Christopher, A. N. (2001).

Excuses and character: Personal and social implications of excuses. Personality and Social Psychology Review, 5, 15–32. doi: 10.1207/S15327957PSPR0501_2 Schmidt, S. (2009). Shall we really do it again? The powerful concept of replication is neglected in the social sciences.

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Turner, J. C., Hogg, M. A., Oakes, P. J., Reicher, S. D., & Wetherell, M. S. (1987). Rediscovering the social group: A Self-Categorization Theory. Cambridge, MA: Basil Blackwell.

Tyler, J. M., & Feldman, R. S. (2007). The double-edged sword of excuses: When do they help, when do they hurt. Journal of Social and Clinical Psychology, 26, 659–688. doi: 10.1521/jscp.2007.26.6.659 Weiner, B. (2005). Motivation from an attribution perspective and the social psychology of perceived competence. In A. J. Elliot & C. S. Dweck (Eds.), Handbook of competence and motivation (pp. 73–84). New York, NY: Guilford Press.

Yee, D. K., & Eccles, J. S. (1988). Parent perceptions and attributions for children’s math achievement. Sex Roles, 19, 317–333. doi: 10.1007/BF00289840

Received January 1, 2015 Revision received June 19, 2015 Accepted June 22, 2015 Published online February 29, 2016 Jade S. Jenkins Department of Institutional Data Management Texas A&M University Texarkana, TX 75503 USA Tel. +1 (630) 217-7484 E-mail jjenkins1@tamut.edu

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New, insightful theory and research concerning reactance processes Topics covered include • Reactance theory in association with guilt appeals • Tests to study the relationship between fear and psychological reactance • The influence of threat to group identity and its associated values and norms on reactance • Benefit of reactance research in health psychology campaigns • Construction and empirical validation of an instrument for measuring state reactance (Salzburger State Reactance Scale) • Motivation intensity theory and its implications for how reactance motives should convert into effortful goal pursuit

Sandra Sittenthaler / Eva Jonas / Eva Traut-Mattausch / Jeff Greenberg (Editors)

New Directions in Reactance Research (Series: Zeitschrift für Psychologie – Vol. 223) 2015, iv + 76 pp., large format US $49.00 / € 34.95 ISBN 978-0-88937-479-9 Psychological reactance theory, formulated by Jack Brehm in 1966, is one of the most popular social psychological theories explaining how people respond to threats to their free behaviors and has attracted attention in both basic and applied research in areas such as health, marketing, politics, and education.

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A review article published 40 years later by Miron and Brehm pointed out several research gaps. That article inspired the editors to develop this carefully compiled collection presenting recent research and developments in reactance theory that both offer new knowledge and illuminate issues still in need of resolution.

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Original Article

Preaching to, or Beyond, the Choir The Politicizing Effects of Fitting Value-Identity Communication in Ideologically Heterogeneous Groups Maja Kutlaca, Martijn Van Zomeren, and Kai Epstude Department of Psychology, University of Groningen, The Netherlands Abstract. Although values motivate participation in collective action, little is known about whether their communication by a social movement motivates identification with it. In the context of student protests against budget cuts, we tested whether and how fitting a value (right to free education) to two relevant group identities (i.e., student vs. national identity) influenced politicized identification among individuals in ideologically different student subgroups (N = 168). Specifically, for students who shared the movement’s ideological background, we found that communicating values increased the predictive power of affective predictors of politicized identification over instrumental ones. However, for students who did not share the movement’s ideological background, fitting values to student (but not national) identity decreased politicized identification. These findings imply that value-identity fit must be taken into account if one wants to motivate a broad audience of potential followers with diverse ideological backgrounds for collective action.

Keywords: social identity, values, communication, politicized identity, collective action

Social movements sometimes succeed in gathering the support of many people (e.g., the civil rights movement; McAdam, 1982). A key explanation for this lies in the manner in which movements communicate their goals to different audiences in an effective way. This is important because effective communication of who they are (i.e., their identity) and what they stand for (i.e., their values) may help movements to motivate not only those who already value what the movement values, but also those in the disadvantaged group who do not necessarily share the movement’s values (i.e., the larger mobilization potential). This raises the question of how social movements may effectively communicate their values and identity in order to motivate a broad audience with diverse ideological backgrounds. This question is particularly relevant in the context of incidental or situation-based disadvantage (Van Zomeren, Postmes, & Spears, 2008), where there is often no already established activist organization that can influence the process of mobilization in a top-down manner.

We seek to answer this question by building on theory and research on the motivational power of values and group identities because these constitute powerful motivators of individual (Rokeach, 1973) and collective behavior (Klandermans, 1997; Van Zomeren, Postmes, & Spears 2012; Van Zomeren, Postmes, Spears, & Betache, 2011).

Specifically, we focus on the communication of values and their motivational effects in ideologically diverse subgroups. For instance, student organizations may communicate that governmental budget cuts on higher education

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imply that the value of free education is being violated in order to increase the perceived illegitimacy of the situation and followers’ identification with the action group (which we refer to as politicizing effects; indeed, politicized group identification is a strong predictor of collective and social movement participation; Simon et al., 1998; for a metaanalysis, see Van Zomeren et al., 2008). However, little is known about whether such a focus on values will have the same politicizing effects on those who already share movement values (preaching to the choir) and on those who do not (preaching beyond the choir).

We suggest that, when preaching to or beyond the choir, communicating a value-identity fit is important for politicization. We experimentally tested this proposal by manipulating how a social movement communicated a value and a relevant group identity, and measured their politicizing effects among Dutch students in the context of budget cuts for higher education (an issue that also arose in, for instance, the UK and Germany in recent years; e.g., Tausch & Becker, 2013). The student movement emerged in a bottom-up manner in response to the government’s policy and was comprised of various locally operating groups at each university. On the basis of a pilot study, we distinguished between two subgroups of students with ideological backgrounds that fit or did not fit that of the movement. We then experimentally manipulated the contextually relevant value (the right to free education) and two contextually relevant identities (student or Dutch identity) that could be fitted to the value. Below, we develop our line of thought and

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specific expectations and then report the pilot study and the experiment.

Politicizing Effects of Value-Identity Communication From a psychological perspective, many different actions can be considered collective actions, ranging from signing a petition to participating in massive demonstrations and occupations of public spaces. The defining feature of these acts is that they are undertaken as group members and aimed at improving the group’s (rather than the individual’s own) position (Van Zomeren et al., 2008; Wright, Taylor, & Moghaddam, 1990). For this reason, identification with their group is a powerful predictor of whether individuals are willing to act on behalf of it (e.g., Tajfel & Turner, 1979). Theory and research on collective action distinguishes between identification with the general social category (e.g., race, gender, or ethnicity) from identification with social movement organizations (often referred to as politicized identification), the latter of which is typically most predictive of social movement participation (Van Zomeren et al., 2008). This is because in a larger societal context, collective action represents an intergroup power struggle where a politicized identity symbolizes a conscious choice on the part of the individual to enter the political arena (e.g., to become a feminist, or environmental activist; Simon & Klandermans, 2001). The more strongly individuals become politicized, the higher is their intrinsic motivation to act on behalf of their group (Stürmer & Simon, 2004).

However, in the context of suddenly imposed grievances (Van Zomeren et al., 2008; Walsh, 1981, 1987), there is often no social movement organization (such as Greenpeace or Blank Panthers), with clear goals which potential followers can identify with. Nevertheless, a movement may arise and gain support when individuals come to realize that they share similar views on the issue (McGarty, Bliuc, Thomas, & Bongiorno, 2009) and are effective in communicating their beliefs to other members of their group. However, one cannot a priori assume that all members of the disadvantaged group are supportive of a movement that aims to represent them (Becker & Wagner, 2009) because they may not share movement’s values.

Previous literature distinguished between affective and instrumental antecedents of politicized identities (Mazzoni, van Zomeren, & Cicognani, 2015; Van Zomeren, 2013).

Politicization is more likely when individuals experience the unfairness and anger about the group’s disadvantage more strongly (Simon & Klandermans, 2001) and/or when individuals more strongly believe that their group is capable of achieving social change (i.e., group efficacy beliefs; Bandura, 1997; Van Zomeren et al., 2008). Values have an important place in this motivational picture because they often define what individuals deem to be unjust and what their relevant goals are (e.g., Skitka & Bauman, 2008; Tetlock, Kirstel, Elson, Green, & Lerner, 2000). Moreover, values that reflect subjectively absolute principles (such as Social Psychology 2016; Vol. 47(1):15–28

human rights; Mazzoni et al., 2015) may transcend existing personal or group identities, because violations of such absolutist values have strong motivational consequences (Van Zomeren et al., 2012). On one hand, values can facilitate politicization as a fit between violated values (e.g., governmental cuts on higher education) and politicized identities geared toward the same issue (e.g., identifying as a student that opposes those governmental measures) can transform an individually held value into a collectively moralized basis for collective action (Van Zomeren et al., 2012).

This suggests that movements may increase their mobilization potential by making salient the relevant value and the relevant group identity in their communication. In other words, communicating values and identities may help movements to create a sense of common cause that will appeal to the majority of group members, which is the first step in the mobilization process (Klandermans, 1984). Only once this is achieved, movements can focus on increasing motivation and on removing potential obstacles to participation. On the other hand, communicating values may not always have the desired effects depending on the ideological background of the audience, as movements can engage in communication with those who already share their values (preaching to the choir) or those who do not (preaching beyond the choir).

Different Politicizing Effects for Different Audiences Social movements typically attempt to change public opinion, including those who do or do not already value what the movement values (Gamson, 1992; Klandermans, 1997). Theory and research suggests at least two ways through which public opinion can be affected: (1) directly increasing or decreasing relevant attitudes (i.e., mean-level changes) or (2) more indirectly by changing the processes leading to a certain attitude (i.e., qualitative changes or changes in the meaning of a certain attitude without necessarily mean-level changes; see Druckman, 2001; Nelson & Garst, 2005; Nelson, Oxley, & Clawson 1997; Slothuus, 2008). This differentiation is important for present purposes because different audiences may not respond equally to the same value communication. To illustrate, in a study about different framings of welfare bills, Slothuus (2008) observed that among moderately politically aware individuals, policy messages increased the support in line with the frame through introduction of novel arguments (i.e., mean-level change). In contrast, among highly politically aware individuals, policy messages changed the predictive power of existing arguments or the meaning of a certain policy in line with the frame (i.e., qualitative change in the policy meaning). This suggests that, in the context of social movements at least, value communication may also have different effects among the audience that may or may not share the movement’s values.

We thus examined two ways in which communicating values can have politicizing effects. First, we tested whether 2015 Hogrefe Publishing

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value communication increases motivation to participate in a social movement action (i.e., by looking at the mean-level changes). This reflects a direct way by which values may operate psychologically by increasing politicized identification. Second, we also tested whether values affect individuals’ motivation indirectly by affecting the relative predictive weights of affective and instrumental antecedents of politicized identification (see also Mazzoni et al., 2013; Van Zomeren et al., 2008).

More specifically, we hypothesized, first, that communicating that important societal values are being transgressed may not directly increase politicized identification when ‘‘preaching to the choir’’ because those individuals will already perceive their values to be violated. Still, we expect that communicating values may make individuals’ affective, rather than instrumental, motivations more important in predicting politicized identification. Indeed, Van Stekelenburg, Klandermans, and van Dijk (2009) found that protesters’ instrumental motivation appeared more important for those mobilized by the labor union (an instrumental movement), whereas perceived unfairness appeared more important for those mobilized by a value-based movement.

Thus, our first hypothesis is that communicating values to ‘‘the choir’’ has indirect but no direct politicizing effects among those who already value what the movement values.

However, when ‘‘preaching beyond the choir,’’ communicating values is unlikely to have any politicizing effects.

In fact, talking about values may even decrease the perception of a common ground between ideologically opposed parties (Kouzakova, Ellemers, Harinck, & Scheepers, 2012). Nevertheless, the effects of values may depend on the identities made salient in the message put forward by the movement. For example, in the context of governmental cuts on higher education, this means that one could fit the right to education to student identity (the disadvantaged group in this context), or to Dutch identity (the larger societal group in this context). Indeed, theory and research on politicization (Simon & Klandermans, 2001) and recategorization (e.g., Turner, Hogg, Oakes, Reicher, & Wetherell, 1987; see also Gaertner, Dovidio, Anastasio, Bachman, & Rust, 1993) suggest that aligning the disadvantaged group’s identity to national identity may increase movement’s mobilization potential (Simon & Klandermans, 2001). Simon and Klandermans (2001) argued that disadvantaged groups seeking to win public support must emphasize their membership within the larger category because that entitles them with equal status and treatment. Such dual identification also facilitates participation in collective action among the disadvantaged group members as evidenced by Turkish immigrants living in Germany (Simon & Ruhs, 2008).

We extended this idea to a new type of audience, namely the members who have a different ideological background within the disadvantaged group. By framing students’

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struggle as violation of a value important to the society as a whole (compared to the students only), we were able to explore whether and how a value-identity fit may have politicizing effects when ‘‘preaching beyond the choir.’’

Overview of Studies We tested our ideas in a pilot study and a follow-up experiment. Through the use of an experimental design we were able to control the specific content of value-identity message (which increases internal validity). Through the use of the real-life student context we could target psychologically meaningful subgroups with different ideological backgrounds (which increases external validity). We took advantage of Dutch students’ protests during 2011 and 2012 occurring after the introduction of governmental budget cuts for higher education (that led to fines for ‘‘slow’’ students and the elimination of students’ free access to public transport). Several bigger student unions managed to coordinate and organize one nation-wide event (i.e., demonstration in The Hague in January 2011) not resulting in any change, while most of the protests took place locally at each university organized by different student groups operating locally. Within this context, value communication referred to these measures not only as a collective disadvantage for students but also as a violation of the right to free education.1 We first conducted a pilot study to (a) validate our assumption that different subgroups of students who share or do not share the movement’s ideological background can be identified, and to (b) pretest the value-identity manipulation within such a diverse sample. We reasoned that these aims were important because they would allow us to effectively focus on two clearly different subgroups in the follow-up experiment, and to evaluate and possibly improve our manipulation.

We note that the manipulation was not designed to reflect a rich, real-life mobilization attempt that one may recognize from movement campaigns. The aim was to focus specifically on the messages that either contain or do not contain values which enabled us to ‘‘cleanly’’ differentiate this type of communication from potential others such as making group identity salient or not (which was held constant) or using highly affective language to increase anger. We only mentioned the value (the right to free education) and the student situation (budget cuts) and left to our participants to deduce that a violation has occurred without suggesting that our participants should feel angry or outraged in any way. By opting for a very subtle manipulation and not explicitly stating a value violation, we increased internal validity but also offered a rather conservative test of our hypotheses.

Under the European Convention on Human Rights the right to free higher education is only an ideal (unlike free basic education which is considered obligatory) and it is left to each nation state to interpret it accordingly (United Nations Human Rights, 1966). In the Netherlands, the universities do charge an entrance fee, so the goal of free higher education is less realized as it is, for example, in Germany, Finland, or Sweden. Thus, imposing additional fees on students seems as moving further away from the internationally held objective.

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Pilot Study Method The sample consisted of 98 bachelor and master students (45 females, Mage = 22.04,2 SD = 3.15), from different faculties (social sciences, law, economics, natural sciences) of the University of Groningen. Participants were approached in university canteens and asked to fill in the questionnaire and as a reward for their participation they were offered money (€3).

Manipulation and Measures There were three versions of the questionnaire that reflected the three conditions of the value manipulation (value/context-only/empty-control condition). In the context-only condition, participants read an article describing that, during 2010 and 2011, the Dutch government announced budget cuts for higher education and that, in response, in January 2011 there was a large protest in The Hague. In the value condition, this information was preceded by an introductory paragraph describing education as a basic right and its importance to the Dutch society in general, thus making the superordinate identity salient (see Supplementary Material). After reading the text, participants responded to two information-check questions that assessed if they had understood the text (e.g., what were the government’s plans regarding the budget for education and the reason for fining students). A manipulation check question asked if any of the following three things was mentioned in the article: ‘‘the education being universal and basic human right’’ (the correct answer for the value condition), ‘‘some faculties closing down’’ (which was not mentioned at all), and ‘‘none of the above’’ (the correct answer for context-only condition). In the empty-control condition, participants did not read any text, but were asked to fill in the dependent measures; this condition served to tap baseline attitudes and motivation to participate in collective action.

Participants then answered questions with standardized response scales (7-point Likert-type scales, with anchors 1 = Not at all to 7 = Very much). First, we measured the intentions to join collective action3 (eight items, e.g., ranging from signing an online petition, to joining a demonstration, boycotting lectures, and occupying a building, a = .91), followed by identification with the politicized group (four items, e.g., ‘‘I identify with the students who oppose these measures’’, a = .90). We focused on students who opposed the austerity measure as broadly indicating

2 3 4 5

the politicized group as there were many different student organizations trying to motivate and coordinate students for actions.

Furthermore, we also measured students’ identification with the Dutch society (four items, e.g., ‘‘I identify with the Dutch society’’ a = .85). As an indicator of instrumental motivation, we included a four-item measure of group efficacy (e.g., ‘‘I think that students, as group, can stop budget cuts’’; a = .97). Affective motivation4 was operationalized as a combination of perceived illegitimacy and perceived immorality of government’s decisions5 (e.g., ‘‘How fair are the austerity measures placed upon students,’’ ‘‘The decision to cut the budget for higher education is against universal moral values’’ (eight items in total, a = .91).

Finally, participants filled in the demographic questions (age, gender, nationality). They also indicated whether they went to the protests in The Hague (11 participants did) which defined our sample as consisting mainly of potential followers (and not as actual participants such as in Van Stekelenburg et al., 2009).

Results and Discussion Most participants apart from two, responded correctly on information-check questions. However, we encountered a problem with the manipulation check as only seven out of 35 participants in the value-framing condition circled the correct answer. The other 27 participants thought that ‘‘none of the above’’ was mentioned in the text. Thus, they did not misremember the introductory paragraph in the text, but simply did not remember it, which may be related to the minimalistic form the manipulation took. In any event, we decided to include a more explicit check in the follow-up experiment.

With this in mind, we then tested whether value communication had a direct effect on motivation. Mean-level scores on most motivational variables did not significantly differ across conditions (see Table 1). We only found the significant effect of condition on affective motivation, F(2, 95) = 4.76, p = .011, g2 = .09. However, the post hoc comparisons revealed that the participants in the control condition differed from the rest, which was of less interest to us (see Table 1). We then proceeded to identify the ideologically different subgroups. Our strategy was to compare students groups based on their study background,5 as previous research had found ideological differences among students depending on their majors (Guy, 2011). Due to relatively small sample size and no effects of the manipulation, we calculated the mean scores on all variables

One person did not indicate age or gender.

A principal component analysis on action intention scale with oblique rotation yielded a one factor solution explaining 53.94% variance, with the individual item loadings ranging from .52 to .84.

A principal component analysis on affective motivation scale with oblique rotation yielded a one factor solution explaining 53.1% variance, with the individual item loadings ranging from .68 to .86.

We also asked participants to indicate their emotions (anger and contempt) regarding the students’ disadvantage, though our main expectation was that the manipulation will have an effect on the affective motivation.

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Table 1. Mean scores and standard deviations on dependent variables in three conditions (pretest) Value-context

Politicized ID Dutch ID Affective motivation Instrumental motivation Action intentions Notes. ID = Identification.

Context-only

Empty-control

M

SD

M

SD

M

SD

4.31 4.82 4.56a 3.54 3.53

1.18 1.09 1.12 1.43 1.20

3.87 4.86 4.14ab 3.17 3.10

1.58 0.97 1.32 1.59 1.60

3.78 4.74 3.67b 3.41 2.99

1.61 1.06 0.99 1.48 1.30

ab

The different superscripts imply statistically significant differences between the groups.

Table 2. Mean scores and standard deviations for students from different faculties pulled across all the conditions (pretest) Social sciencesa

Politicized ID Dutch ID Affective motivation Instrumental motivation Action intentions

Economicsb

Lawc

Natural sciencesd

M

SD

M

SD

M

SD

M

SD

4.55 4.78 4.35 3.58 3.66

1.49 1.15 1.26 1.40 1.34

3.69 4.72 3.83 3.39 2.94

1.54 1.10 1.27 1.55 1.45

4.17 4.95 4.24 2.88 3.18

1.29 1.14 1.18 1.42 1.70

3.93 4.70 4.39 3.56 3.42

1.45 0.76 0.99 1.73 1.03

Notes. an = 23; bn = 31; cn = 15; dn = 21. ID = Identification; CA = Collective action.

collapsing over the three conditions. Overall, the economics students seem to be the least supportive of student protest in contrast to social sciences students who on average were the most motivated (see Table 2). The contrast test comparing those social sciences and economics students indicated that these two samples differed in their intentions to act t(52) = 1.87, p = .068, and politicized identification, t(52) = 2.08, p = .04, suggesting that these two groups would be fairly good representatives of different audiences.

We note that these findings are in line with observations

by Fiske, Kitayama, Markus, and Nisbett (1998) and previous studies showing differential support of welfare policies (Guy, 2011) and system-justifying ideologies (Pratto, Sidanius, Stallworth, & Malle, 1994) among students of social sciences and economics. To corroborate this choice, we decided to include specific measures of ideological background. In sum, the pilot study suggested that our choice of context and group suited our aims, but also pointed to potential improvements with an eye on the follow-up experiment.

Experiment The experiment’s main aim was to test whether value communication would have politicizing effects both within and beyond the movement’s own ‘‘choir.’’ Furthermore, in the follow-up experiment we manipulated whether the value message was embedded in a student or national identity, in order to test the notion of value-identity fit. We wanted 2015 Hogrefe Publishing

to explore whether communicating values as embedded in a national identity may have politicizing effects when ‘‘preaching beyond the choir,’’ whereas we expected indirect rather than direct politicizing effects when ‘‘preaching to the choir.’’

Method Participants and Design The sample consisted of 181 students. We excluded 13 students from the analysis because they either indicated they did not have the Dutch nationality or did not fill in the nationality question; one student did not fill in his educational background. Participants were approached in canteens, libraries, and lectures at either the social sciences or at the economics faculty and asked to fill in the questionnaire. Six students did not originally belong to either of the two (they were students of natural sciences), but were still included in the final sample and assigned to a study based on the location they were approached. The data were collected among bachelor and master students (Mage = 21.51, SD = 2.35; 68 men, 100 women). Only 19 students participated in any student protests organized in the past years, which confirmed that our sample consisted of potential followers. The experimental design was a 2 (Subgroup of students: social sciences vs. economics) · 4 (Value communication: value-student identity vs. value-national identity vs. context-only vs. empty-control condition) between-subjects design.

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Manipulation In order to create a fit between violation of the right to education and student and national identity the wording of the first sentence was different in those conditions: ‘‘Modern Dutch society is based on the principles of freedom and equality’’ versus ‘‘Most students value the principles of freedom and equality.’’ With this subtle reformulation, we defined the same value as embedded in the national (Dutch) or group (students) identity. The last paragraph in both conditions was slightly changed to reflect the most recent changes in the governmental plans (after the failed negotiations during the summer, the first generation of students was obliged to pay the fine starting from September6).

Again, the design also included the context-only and an additional empty-control condition where people were asked to fill in the dependent variables. Adding these two conditions enabled us to test, for either those who already share or do not share the movement’s ideological background, both (a) mean-level effects of value-identity communication (i.e., whether mentioning a value would increase politicized identification) and (b) its qualitative effects (i.e., whether mentioning a value would increase the relative predictive strength of affective motivation and national identification).

Information and Manipulation Check The information checks were the same as in the pilot study.

However, we reformulated the manipulation check by referring specifically to the opening sentence of the article.

Participants could choose between three options, that is, the opening sentences of the two value conditions, plus ‘‘none of the above’’ which was correct for the context-only condition.

Dependent Variables We used the same scales regarding action intentions, identification, affective and instrumental motivation as used in the pilot study. Furthermore, in order to support our assumption that economics and social sciences students differ in their ideological views we included a number of new scales.7 First of all, based on a system justification scale by Jost and Hunyady (2003) and a protestant work ethic scale

by Ghorpade, Lackritz, and Singh (2006) we created a short 6-item scale tapping into system-justification beliefs (e.g., ‘‘Most people who don’t get ahead in our society should 6 7

8

not blame the system; they have only themselves to blame’’; a = .81; a principal component analysis with an oblique rotation extracted only one factor explaining 51.3% of the variance, with all factor loadings > .68). Next, we included two bipolar items measuring political orientation (from 1 = Progressive to 7 = Conservative and 1 = Left to 7 = Right) and participants’ opinion about the necessity to cut on welfare in times of crisis (two items, a = .73).

Finally, we asked the students what would be the appropriate size of the fine if they were asked to determine it (the answers ranged 1 = Less than 500 Euros to 5 = 2,000– 3,000 Euros, increasing by 500 Euros apart from the last step). These measures enabled a more specific interpretation of any difference between the subgroups of students we chose to sample.

Results Information and Manipulation Check The number of participants who failed the manipulation check was significantly smaller in this study (12 students or 9.5%). Some students made a mistake on one of the information-check questions, but did not fail the manipulation check. Considering that we collected the data at canteens and lectures, overall a large majority of the sample responded correctly to all information-check and manipulation check questions (77.6%), therefore we ran the analyses on the whole sample.8

Sample Differences Verifying assumptions regarding different subgroups’ overall ideological background, results showed that economics students were more right-wing (Meconomics = 4.51, SD = 1.49 vs. Msocialsciences = 3.20, SD = 1.36), F(1, 164) = 34.76, p < .001, g2 = .18, and endorsed system-justifying ideologies to a larger extent than social sciences students (Meconomics = 3.81, SD = 1.02 vs.

SD = 1.10), F(1, 163) = 14.07, Msocialsciences = 3.20, p < .001, g2 = .08. Although both subgroups described themselves as being relatively progressive rather than conservative (Meconomics = 3.23, SD = 1.39 vs. Msocialsciences = 3.07, SD = 1.39), economics students perceived the budget cuts for welfare as more justified in times of crisis (Meconomics = 3.69, SD = 1.35 vs. Msocialsciences = 3.14, SD = 1.31), F(1, 165) = 7.15, p = .008, g2 = .04, and thought that

A month after our data collection the government decided to withdraw this fine. This was the result of political negotiations and elections that took place just after our data collection and not the result of the successful student protest.

In some countries economics is also considered as social sciences. However, at University of Groningen economics faculty is separate from the social sciences faculty and is actually part of the natural sciences campus. This of course does not immediately imply that they have different political preferences, but they do not attend the same lectures as other social scientists and are exposed to different types of thinking about the social welfare issues.

We also compared the participants who answered all the questions correctly with the ones who made mistakes and there was no difference found on any of the collective action or ideological variables. The only difference that emerged was on the identification with the Dutch society, where participants who responded correctly had somewhat higher scores: Mcorrect = 5.24, SD = 1.02 versus Mincorrect = 4.80, SD = 1.02, F(1, 166) = 4.3, p = .04.

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Table 3. Mean scores and standard deviation for social sciences and economics and business students (main study) Value-student identity M Politicized ID Dutch ID Affective motivation Instrumental motivation Action intentions

3.94 5.01 4.57 3.63 3.40

Politicized ID Dutch ID Affective motivation Instrumental motivation Action intentions

3.21 5.21 3.53a 2.81 2.28

SD

Value-national identity M

SD

Social sciences (n = 85) 1.18 3.80 1.46 0.69 5.39 0.84 0.97 4.25 1.01 1.20 3.21 1.54 1.15 2.94 1.33 Economics and business (n = 83) 1.55 3.32 1.35 1.20 4.99 0.99 1.10 4.16b 0.87 1.45 2.89 1.31 1.23 2.69 1.24

Context-only

Empty-control

M

SD

M

SD

4.13 5.09 4.68 2.88 3.11

1.11 0.75 0.71 1.06 1.16

3.93 5.02 4.73 3.25 2.93

1.42 1.52 1.06 1.46 0.98

3.30 5.19 4.37b 2.64 2.39

1.32 1.10 1.06 1.33 1.30

3.85 5.50 4.38b 3.54 3.07

1.23 0.97 1.20 1.63 1.47

Notes. abThe different superscripts imply statistically significant differences between the groups. ID = Identification; CA = Collective action.

students should pay higher fines for prolonging their studies (Meconomics = 2.53, SD = 1.40 vs. Msocialsciences = 2.10, SD = 0.9), F(1, 162) = 5.66, p = .018, g2 = .03. This corroborates the notion of ideologically heterogeneous subgroups within the larger student group. It also corroborates the idea that the social sciences students reflected the movement’s ‘‘choir’’ better than the economics students.

Testing Direct (Mean-Level) Effects In order to examine the effects of our manipulation we conducted a 2 (Education type) · 4 (Condition) analysis of variance (ANOVA). We only found significant differences between two study groups whereby social sciences students had higher action intentions (Msocialsciences = 3.09, SD = 1.15 vs. Meconomics = 2.62, SD = 1.32), F(1, 160) = 6.52, p = .012, g2p = .04, they identified more strongly with the group that opposes the measures (Msocialsciences = 3.95, SD = 1.28 vs. Meconomics = 3.42, SD = 1.36), F(1, 160) = 6.64, p = .011, g2p = .04, and perceived the situation to be more unfair (Msocialsciences = 4.56, SD = 0.94 vs. Meconomics = 4.13, SD = 1.09), F(1, 160) = 8.44, p = .004, g2p = .05.

Instrumental motivation and national identification did not differ between the groups. No other effects were significant. Still, as the main hypotheses regarding the effects of communication were formulated depending on the type of audience, we also tested whether our manipulation had effects on the issue supporters and issue opponents separately.

As expected, among the social sciences students, valueidentity communication did not directly influence any of the dependent variables (see Table 3). Thus, although there 9

was a clear value-identity fit, the communication of this fit did not have politicizing effects at the mean-level.

Among the economics students, we found a hint at a direct value-identity effect on affective motivation F(3, 79) = 2.67, p = .053, g2p = .09. Inspection of the means shows that communicating a violation of a human right as a part of the normative content of the student identity decreased the affective motivation compared to when national identity was made salient or when values were not communicated at all. Post hoc analysis using the least significance difference (LSD) method confirmed the differences between the value-student identity condition and the other conditions.9 However, in contrast to our expectation, communicating the same value violation as embedded in the national identity did not significantly increase the affective motivation or other motivational indicators compared to the context-only or empty-control condition.

Indirect Effects (Regression Analyses) To test whether predictors of politicized identification depend on the type of communication, we first ran multiple regression analyses predicting politicized identification and action intentions including both samples. However, our main hypothesis was formulated depending on the type of audience and these regressions will be the main focus of our analyses. All regression analyses were conducted in the same order: in the first step, we included three dummy variables separating the value-student, context-only, and control conditions. Hence, the value-nation condition served as a baseline. In the second step, we included the relevant predictors (national identification, affective and instrumental motivation), followed by interactions between

We note that among the economists, the control group had consistently higher scores compared to others. We believe that this is due to the difference in age: namely, there were a larger number of first year students in this condition and the average age was lower than the average of the whole sample (20.1 compared to 21.5).

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7

Politicized Identification

Value-National Condition 6

Value-Student Condition

5 4 3 2 1

Low National Identification

High National Identification

Figure 1. Interaction plot examining differences in politicized identification among the students (averaged across both samples) with low ( 1 SD) and high (+1 SD) on scores on measure of national identification. The data for plotting was taken from the third step in regression analysis. our manipulations and predictors of politicized identification. In the final regression analysis on action intentions we also added politicized identification as a predictor to test whether, in line with the literature, politicized identification predicted action intentions.

First, there were no differences between the baseline and the other three conditions (value-student condition B = 0.06, t(164) = 0.21, p = .832; context-only B = 0.19, t(164) = 0.66, p = .509; empty-control B = 0.35, t(164) = 1.21, p = .228). In the second step, the national identification (B = 0.22, t(161) = 2.75, p = .007), affective motivation (Step 2, B = 0.73, t(161) = 8.24, p < .001), and instrumental motivation (Step 2, B = 0.13, t(161) = 1.91, p = .059, marginally significant) positively predicted politicized group identification. There was a marginally significant interaction between value-student condition and national identification (Step 3, B = 0.49, t(158) = 1.90, p = .059). In order to unpack this interaction, we conducted a simple slope analysis (see Figure 1).

The more students identified with their nation, the higher they identified with the group that opposes the budget cuts when value was communicated as part of the national identity, B = 0.34, t(158) = 1.99, p = .048). But in contrast, there was no relationship between national and politicized identification (the slope was even in the opposite direction) when the value was communicated as part of the student identity B = 0.15, t(158) = 0.78, p = .43.

In the regression analysis on collective action intentions, again there were no differences between the baseline and the other three conditions (value-student condition 10 11

B = 0.08, t(164) = 0.27, p = .786; context-only condition B = 0.03, t(164) = 0.12, p = .904; empty-control condition B = 0.19, t(164) = 0.7, p = .485). We found only the main effects of affective motivation (Step 2, B = 0.20, t(160) = 2.20, p = .03), instrumental motivation (Step 2, B = 0.16, t(160) = 2.77, p = .006), and politicized identification B = 0.48, t(160) = 7.01, p < .001) and no interaction effects suggesting that our manipulation did not influence action intentions.10 Hence, as a follow-up, we only repeated the regression analysis on politicized identification in the two samples, as previous analysis and our theoretical reasoning revolved around the effects of communication on politicized identification rather than action intentions (for more details, see Supplementary Materials).

For economics students, the regression analysis rendered similar results to the one obtained on the whole sample.

Again, there were no differences between the baseline and other conditions, but national identification (Step 2, B = 0.25, t(76) = 2.07, p = .042), affective motivation (Step 2, B = 0.61, t(79) = 4.47, p < .001), and instrumental motivation (Step 2, B = 0.18, t(76) = 1.75, p = .084, marginally significant) positively predicted politicized identification (see Table 4). However, more importantly and in line with our expectations, there was a significant interaction between type of values communicated and national identification, B = 0.88, t(73) = 2.66, p = .01 (Step 3). Thus, depending on the identities made salient, the value communication increased politicized identification11 by appealing to the national identity (B = 0.51, t(73) = 2.26, p = .027) or decreased it by appealing to the groupâ&#x20AC;&#x2122;s identity, though this effect was not statistically significant (B = 0.37, t(73) = 1.57, p = .12). For more details, see Figure 2.

For social sciences students, affective motivation was the main predictor of politicized identification B = 0.83, t(78) = 6.82, p < .001 (Step 2, see Table 5). Thus, communication of value violation allowed for a stronger psychological basis of politicized identity in terms of affective concerns (which reflects the findings by Van Stekelenburg et al., 2009, to some extent). However, when the value was not communicated, the relation between the two variables changed, as evidenced by a negative slope for the interaction between context-only dummy and affective motivation B = 0.96, t(73) = 2.51, p = .015 (Step 4). Namely, when the value was communicated the affective motivation strongly predicted politicized identification B = 1.16, t(73) = 5.11, p < .001, while there was a very weak and a nonsignificant relationship between the two variables when the value was omitted from the communication B = 0.19, t(73) = 0.62, p = .54. Still, identity-value fit effects were much stronger among the economics students, directly influencing the relationship between the two identities (Figure 3).

In the regression analysis emerged a marginally significant interaction between national identification and the control condition B = 0.46, t(157) = 1.51, p = .058. However, as this was an empty condition, we cannot say what exactly influenced the responses.

Next to politicized identification, the value-identity (mis)fit also affected the relation between national identification and affective motivation. Namely, national identification was negatively related to affective motivation in the value-student identity condition, r(16) = .53, p = .025, while there was no relationship (or even a positive one) between the two variables in the value-national identity condition, r(22) = .20, p = .34. The difference between correlations was significant, Fisherâ&#x20AC;&#x2122;s z = 2.35, p = .02.

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Table 4. Regression analysis predicting politicized identification among economics students

Value-student condition Context-only condition Control condition Dutch ID Affective motivation Instrumental motivation Interaction terms Value-student condition · Dutch ID Context-only condition · Dutch ID Control condition · Dutch ID Value-student condition · Affective motivation Context-only condition · Affective motivation Control condition · Affective motivation Value-student condition · Instrumental motivation Context-only condition · Instrumental motivation Control condition · Instrumental motivation F df p R2 adjusted R2 change p change

Step 1

Step 2

B

B

SE

0.12 0.42 0.02 0.41 0.52 0.41

SE

0.23 0.16 0.14 0.25* 0.61*** 0.180

0.92 3.79 0.44 0.00

Step 3

0.36 0.34 0.34 0.12 0.14 0.10

7.58 6.76 < 0.001 0.33 0.34 < 0.001

B

SE

Step 4

Step 5

B

B

SE

SE

0.10 0.16 0.05 0.51* 0.49*** 0.25*

0.35 0.33 0.34 0.23 0.14 0.10

0.21 0.17 0.09 0.50* 0.53* 0.27*

0.39 0.34 0.34 0.23 0.27 0.11

0.31 0.18 0.05 0.50* 0.480 0.37*

0.40 0.35 0.35 0.23 0.28 0.18

0.88** 0.01 0.20

0.33 0.32 0.34

0.79* 0.02 0.20 0.13 0.00 0.21

0.36 0.33 0.34 0.39 0.36 0.34

0.56 0.02 0.22 0.45 0.05 0.27 0.40 0.12 0.01

0.40 0.34 0.35 0.46 0.38 0.43 0.31 0.27 0.30

6.59 9.73 < 0.001 0.38 0.07 0.03

4.90 12.70 < 0.001 0.36 0.01 0.78

3.99 15.67 < 0.001 0.35 0.02 0.59

Notes. Unstandardized regression coefficients are provided. ID = Identification. 0p < .1. *p < .05. **p < .01. ***p < .001.

7

7 Value-National Condition Value-Student Condition

5 4 3 2 1

6 Politicized Identification

Politicized Identification

6

5 4 3 Value-National Condition

2

Context-Only Condition 1 Low National Identification

High National Identification

Figure 2. Interaction plot examining differences in politicized identification among the economics students with low ( 1 SD) and high (+1 SD) on scores on measure of national identification. The data for plotting was taken from the third step in regression analysis.

General Discussion This research showed different politicizing effects of valueidentity communication within a student movement context in the Netherlands. Our findings suggest that for the audience that already shares the movement’s values, ‘‘preaching 2015 Hogrefe Publishing

Low Affective Motivation

High Affective Motivation

Figure 3. Interaction plot examining differences in politicized identification among the social sciences students with low ( 1 SD) and high (+1 SD) scores on the affective motivation scale. The data for plotting was taken from Step 3.

to the choir’’ with respect to values influenced their motivation only indirectly by creating a stronger link between affective motivation and politicized identification. One way of interpreting this finding is that for these students, their politicized identity became more defined by affective concerns.

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Moreover, for the audience not sharing this ideological background, we found that ‘‘preaching beyond the choir’’ seems sensitive to the notion of value-identity (mis)fit. Specifically, our results suggest that a value-identity misfit may further alienate this audience from the movement that seeks their support (at the mean level). At the correlational level, however, we found support for the idea that a value-identity fit has indirect politicizing effects to the extent that the national identity (and presumably the values embedded in it) became more predictive of politicized identification.

We discuss implications of our findings below.

Theoretical and Practical Implications First of all, our findings complement research on motivational power of values (e.g., Van Zomeren et al., 2011) by looking at how communication of values by social movements influences politicization whereas previous work only looked to what extent participation in collective action was determined by individuals’ values. Hence, together with other recent work (see also Mazzoni et al., 2015) this study offers more explicit evidence that values are the active ingredient in moral motivation to engage in collective action (Van Zomeren, 2013).

Second, the findings also complement research by Van Stekelenburg et al. (2009) by testing both direct and indirect effects of value-identity communication on potential protest participants (rather than actual ones, as in Van Stekelenburg et al., 2009). This is important as the participants in the

study by Van Stekelenburg and colleagues already passed through all four stages of mobilization according to the Klandermans (1984) model and their motives to participate have become crystallized. In contrast, our work is situated in the first two stages of mobilization and shows how movements can create consensus among potential followers by emphasizing values and identities. We move beyond this and other previous research by using an experimental approach, coupled with tests among different subgroups that reflect answers to the question whether preaching to or beyond the choir can have politicizing effects. This is an important issue for theorists, researchers, as well as practitioners of collective action.

Third, our focus on communication between movements and potential followers locates our research at the crossroads between ‘‘micro’’-level perspectives (i.e., psychological work on individuals’ motivation) and ‘‘meso’’- (i.e., sociological work on framing and mobilization context) to studying collective action. One of the core functions of social movement frames is to motivate people by providing reasons for participation (Benford, 1993; Benford & Snow, 2000), and sociological theories of framing assumed that communicating values corresponding with beliefs of the potential followers increases the mobilization potential of a frame. Thus, our findings provide support for this assumption among those who share the movement’s values, but importantly specify how (and for whom) such framing effects come about psychologically.

Fourth, another important implication of the current work is the analytical and empirical differentiation between

Table 5. Regression analysis predicting politicized identification among social sciences students Step 1

Step 2

B

B

SE

Value-student condition 0.14 0.41 Context-only condition 0.33 0.40 Control condition 0.13 0.40 Dutch ID Affective motivation Instrumental motivation Interaction terms Value-student condition · Dutch ID Context-only condition · Dutch ID Control condition · Dutch ID Value-student condition · Affective motivation Context-only condition · Affective motivation Control condition · Affective motivation Value-student condition · Instrumental motivation Context-only condition · Instrumental motivation Control condition · Instrumental motivation F df p R2 adjusted R2 change p change

0.22 3.81 0.88 0

0.10 0.04 0.21 0.16 0.83*** 0.09

Step 3 SE 0.32 0.32 0.32 0.11 0.12 0.09

9.64 6.78 < 0.001 0.38 0.42 < 0.001

Step 4

B

SE

Step 5

B

SE

B

SE

0.15 0.00 0.25 0.00 0.83*** 0.08

0.33 0.33 0.33 0.28 0.13 0.09

0.26 0.01 0.38 0.01 1.16*** 0.11

0.33 0.33 0.33 0.27 0.23 0.09

0.29 0.04 0.40 0.06 1.18*** 0.09

0.34 0.34 0.33 0.28 0.23 0.15

0.11 0.30 0.18

0.44 0.41 0.32

0.08 0.39 0.16 0.550 0.96* 0.16

0.43 0.40 0.31 0.32 0.38 0.31

0.14 0.50 0.18 0.590 1.06** 0.22 0.23 0.36 0.33

0.44 0.41 0.32 0.34 0.40 0.31 0.26 0.26 0.23

6.29 9.75 < 0.001 0.36 0.00 0.90

5.67 12.73 < 0.001 0.40 0.06 0.06

4.74 15.7 < 0.001 0.40 0.02 0.40

Notes. Unstandardized regression coefficients are provided. ID = Identification. 0p < .1. *p < .05. **p < .01. ***p < .001.

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direct and indirect politicizing effects of value-identity communication (Druckman, 2001; Slothuus, 2008). The former refers to mean-level increases or decreases in specific motivations as a function of communication, whereas the latter refers to shifts in the predictive power of specific motivations with respect to politicized identification (i.e., shifts in the psychological meaning of that identity). Looking at both effects at the same time broadens our understanding of communication between movements and their audiences. For instance, for those already sharing the movement’s ideological background, making values salient allows for affective motivation to become more important in defining politicized identity. In contrast, for those not sharing the movement’s values, embedding the value in the ‘‘right’’ identity can overcome potential detrimental effects of value-laden messages and allow for the relevant broader identity to define the politicized identity.

We believe that, at least for those who already share the movement’s ideology, value-identity communication in essence implies communicating a group norm that revolves around feelings of unfairness and anger. This is important as it effectively reduces individuals’ reliance on instrumental motivations that may be characterized as opportunistic.

Such a shift is in line with the idea that a politicized identity may be created through the alignment of group norms for group emotions such as anger and outrage (Thomas, McGarty, & Mavor, 2009). Nevertheless, the work by Thomas et al. (2009) suggests that social interaction with similar-minded individuals is necessary to increase individuals’ motivation for collective action, which makes it quite different from the current focus on one-sided communication (from movements to the audience). Future research may examine whether communicating values may actually become effective at the mean-level when individuals can discuss their values and identity with similar-minded others.

However, movements have to be very sensitive in communicating their goals to an ideologically opposed group.

For example, for the audience (i.e., economics students) that puts greater personal (rather than group) responsibility for misfortune and showed support for welfare cuts in times of crisis, a message that places an additional emphasis on the students as the inclusive group being deprived of important rights offered little common ground. This fits with the work by Sassenberg, Kessler, and Mummendey (2003) who also showed that important psychological differences (e.g., promotion vs. prevention focus) go hand in hand with the values embedded in different majors or professions (orientation toward profit maximization among business majors vs. orientation toward inequality prevention among law majors). Moreover, it also corroborates our choice of economics students as a proxy of relatively more conservative group among students.

Consequently, one implication of our findings would be to simply avoid any type of value communication toward ideologically different groups. Such avoidance specifically reduces the risk of alienating a subgroup through a value-identity mismatch. However, it is doubtful whether this is a fruitful strategy in the long run because values

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are essential to identity, and identity is essential to social movements especially in the contexts of incidental disadvantage where the identity needs to be created bottom-up.

In our view, our study points that a potentially more successful strategy is to link the value to national identity (or a similar type of superordinate identity) which opens the possibility, at least indirectly, for a movement’s cause to be seen as contributing to the wider society and therefore worthy of support.

This directly ties in with work on politicized identities.

For instance, according to Simon and Klandermans (2001), national identity is seen as one of the main antecedents of the politicized collective identity as it provides ‘‘the context for shared grievances, adversarial attribution and the ensuing power struggles for social change’’ (p. 326). Other studies have also noted the mobilizing power of the national identity by looking at speeches of political leaders who call upon ‘‘national values’’ to justify discrimination against other minorities (Verkuyten, 2013). In other words, fitting values to national identity is a strategy that may work well for both right and left wing movements. Thus, our findings are in line with previous research and generalize the process from the usual groups like general public or media to members of ideologically heterogeneous groups.

Finally, the current findings also have practical implications to the extent that they provide specific pointers toward motivating individuals for collective action. First, movements need to consider that ideologically diverse subgroups require different value-identity communication (a point underscored by the finding that a focus on national identity appeared more promising for ‘‘preaching beyond the choir’’). Second, this also means that activists should be flexible in tuning their communication to different audiences in order to mobilize greater number of followers (even if those to be mobilized do not share one’s ideological background). In this sense, aligning the values of the movement with the greater societal goals appears a good strategy, with an eye on that movements’ actions should actually put those goals into practice and not only use it as an effective communication strategy. Moreover, value messages may lead to more long-term motivation as they increase the reliance on affective predictors of politicization that tend to be more stable. Although people care about values, the lack of direct effect of value communication suggests that just talking about values, especially when the struggle is already been going on for a while, is not enough to get people out on the street. Our intuition is that movement practitioners should emphasize individuals’ commitment to act upon their values and provide clear steps to achieve those values, rather than just reminding them of something they already believe in.

Limitations One limitation of the current work concerns its external validity. Political issues may vary greatly with respect to how central are the values for their definition, where some

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such as abortion or gay rights are in their essence value conflicts, whereas others such as budget cuts or increase costs of living may not necessarily be directly related to values.

Still, in countries like Germany or Finland where the right to free higher education is implemented in government policies, one could expect that issues like budget cuts could elicit stronger grievances as the discrepancy between the present ‘‘ideal’’ state and potential change is much bigger compared to the Netherlands where the students already pay entrance fees. In this context, we would assume that value communication may have more direct effects on politicization and participation in collective action. The downside is that in a more polarized value context, people are usually divided in subgroups with firmly established view of the situation and the ones who hold opposite views may completely be irresponsive to the communication. Our findings may apply less to these issues. However, Van Stekelenburg et al. (2009) also found similar patterns among the demonstrators against a reform of early retirement policies attracting 300,000 people in Amsterdam in 2004. This convergence increases confidence in the external validity of the current findings. Future research should try to replicate the current findings in contexts where value conflict is stronger.

Another potential limitation concerns the generalization of the value-identity (mis)fit effects beyond the movements operating within a national level context. In the current political arena, many movements have international agendas and aim to mobilize people from different countries (like the Peace movement or Occupy). Hence, in these situations national identification can have rather debilitating effects on politicized identification. The key point here is that aligning values with higher-order identities can be seen as a general communication strategy. Thus, we would expect similar motivational consequences in aligning values with identities like European or human on people from different countries and ideological backgrounds. This is clearly an important area for future research.

Lastly, we note that a single study with a cross-sectional design obviously cannot capture the richness of real-life discussions between activists and their potential followers.

A longitudinal design encompassing all four stages of mobilization process (Klandermans, 1984) would enable a thorough analysis of changes in followers as well as movements’ goals as a result of the communication. Indeed, our findings only point out to the effects of communication on potential followers, whereas communication is a two-sided process and movements may change their initial goals in order to win the support of various groups. For example, we only focused on the communication between a movement and its immediate target audiences, while movements may also engage in communication with the general public and with the outgroup itself. In any event, we believe that theory and research on collective action would benefit from more frequent use of longitudinal designs (e.g., TurnerZwinkels, van Zomeren, & Postmes, 2015) as they are better able to examine how various identity dynamics relate to participation in collective action.

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Conclusion Our findings suggest that the principle of value-identity fit can be used by social movements in their communication to individuals from different ideological subgroups. As multiple identities and value violations may be relevant in a given social context, the success of value-identity communication ultimately depends on the sensitivity of social movements to the (diverse) ideological backgrounds of their potential followers. The current work shows that it may be fruitful for movements to ‘‘tailor’’ different forms of valueidentity messages to different subgroups, for instance focusing on value violations as embedded in the disadvantaged group identity or in society at large.

Electronic Supplementary Material The electronic supplementary material is available with the online version of the article at http://dx.doi.org/10.1027/ 1864-9335/a000254 ESM 1. Text and tables (PDF).

Supplementary Materials include the exact wording of the manipulation and the regression analyses on politicized identification and collective action intentions conducted on the whole sample (including both social sciences and economics students).

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Received November 20, 2014 Revision received May 12, 2015 Accepted June 30, 2015 Published online December 30, 2015 Maja Kutlaca Department of Psychology University of Groningen Grote Kruisstraat 2/1 9712 TS Groningen The Netherlands Tel. +31 50 363-6248 E-mail m.kutlaca@rug.nl

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Original Article

Do I Shoot Faster Because I Am Thinking about an Outgroup or a Threatening Outgroup?

Shooter Bias, Perceived Threat, and Intergroup Processes Jessica Mange,1 Keren Sharvit,2 Nicolas Margas,3 and Cécile Sénémeaud1 1

Psychology Department, Normandie Université, UNICAEN, NIMEC, Caen, France, 2 Peace and Conflict Studies Department, University of Haifa, Israel, 3 STAPS Department, Normandie Université, UNICAEN, CESAMS, Caen, France

Abstract. This research examines if aggressive responses through a shooter bias are systematically generated by priming outgroups or if a threat stereotypically associated with the primed outgroup is required. First, a pilot study identified outgroups stereotypically associated and not associated with threat. Afterwards, the main study included a manipulation of target group accessibility – ingroup versus nonthreatening outgroup versus threatening outgroup. Following exposure to primes of the group categories, the participants in all conditions played a shooter game in which the targets were males and females with ambiguous ethnicity and religion. Results demonstrated that while only priming of an outgroup stereotypically associated with threat elicits aggressive responses, priming of both nonthreatening and threatening outgroups leads to an increase in the ability to distinguish between stimuli compared to ingroup priming. These effects are discussed in terms of priming effects, dimensions of threat, and possible interpretations of this ability increase.

Keywords: social categories priming, perceived threat, aggressive responses, shooter paradigm

The division of the social world in terms of ‘‘us’’ versus ‘‘them’’ has been shown to appear at least as early as the age of 11 months (Mahajan & Wynn, 2012), and preferences to similar others seem stable across cultures (Allport, 1954/1979). Studies on ethnocentrism classically presumed that positive regard toward one’s ingroup and negativity and hostility toward outgroups are reciprocally related. However, experimental findings support the idea that ingroup favoritism and outgroup derogation are separable phenomena (see Brewer, 1999 for a review). Whereas ingroup favoritism is ‘‘psychologically primary’’ (Allport, 1954), specific conditions are required for outgroup discrimination and intergroup aggression to occur (Struch & Schwartz, 1989). In the present research we investigate whether the priming of outgroups can elicit aggressive responses toward ambiguous targets. While previous research (Mange, Chun, Sharvit, & Belanger, 2012) found increased aggression following the priming of threatening outgroups, in the present research we compare the effects of priming a threatening and nonthreatening outgroup. Given the importance of threat perception in eliciting intergroup hostility (see Riek, Mania, & Gaertner, 2006; Stephan & Stephan, 1996, 2000, for a meta-analysis) or threat cues in eliciting intergroup Ó 2015 Hogrefe Publishing

aggressive responses (e.g., Correll, Wittenbrink, Park, Judd, & Goyle, 2011), we anticipate greater aggression after priming a threatening outgroup.

Measuring Aggressive Responses Toward Outgroups Using the Shooter Bias Aggressive responses toward outgroups can be studied through several methodological paradigms. For example, aggression can be assessed by a posteriori coding of behavioral responses (Bargh, Chen, & Burrows, 1996, Study 3; Chen & Bargh, 1997; Cesario, Plaks, Hagiwara, Navarrete, & Higgins, 2010, Study 2a), or by the amount of painful stimuli inflicted on someone (e.g., strength of electric shock administered, Berkowitz, 1964; amount of spicy sauce given, Mc Gregor et al., 1998; amount and duration of painful noise blasts diffused, Muller, Bushman, Subra, & Ceaux, 2012), or by accessibility of fight-related words (Cesario et al., 2010, Study 1). In the past decade, an original and intriguing method of exploring aggressive responses toward outgroups and the contexts producing such responses has been the shooter paradigm (Correll, Park, Judd, & Social Psychology 2016; Vol. 47(1):29–37 DOI: 10.1027/1864-9335/a000255

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Wittenbrink, 2002). This paradigm relies on a videogame with armed and unarmed targets belonging to different groups. In most cases (e.g., Correll, Park, Judd, & Wittenbrink, 2007; Correll, Park, Judd, Wittenbrink, Sadler, et al., 2007; Correll et al., 2011; Plant, Goplen, & Kuntsman, 2011; Sim, Correll, & Sadler, 2013), the videogame presents Black and White targets embedded in an unpopulated background scene. Results typically reveal a shooter bias (i.e., faster decision to shoot armed targets and/or slower decision not to shoot unarmed targets) toward Black targets. Unkelbach, Forgas, and Denson (2008) extended these results to Muslim targets demonstrating the ‘‘turban effect’’: targets presenting a Muslim appearance (a turban for men and a veil for women) generate a greater bias to shoot than targets without these headdress attributes.

This effect was reinforced by ethnicity and gender of the targets. Specifically, non-Caucasian men wearing a turban generated the greatest shooter bias observed. On the whole, all these studies demonstrate that exposure to an outgroup can increase aggressive responses. However, in most cases, the outgroups toward which aggressive responses were assessed using this paradigm were ones stereotypically perceived as threatening. This led us to wonder whether any outgroup would elicit aggressive responses in a shooter paradigm, or whether this process is unique to target outgroups stereotypically associated with threat.

Previous research points to the decisive role of threat in producing the shooter bias (Correll et al., 2011; Miller, Zielaskowski, & Plant, 2012). Several studies have focused on individual and contextual characteristics that produce aggressive responses. Correll et al. (2011) observed that primes of context threat lower the threshold to shoot. Focusing on individual differences, Miller et al. (2012) suggested that the shooter bias can be observed for any outgroups among individuals prone to seeing the world as dangerous and to assuming that all outgroups are threatening. They demonstrated that outgroups – whether threatening or not – generated more errors in the decision not to shot unarmed targets, but only among individuals with a strong belief in interpersonal threat (Altemeyer, 1988). One study (Sadler, Correll, Park, & Judd, 2012) focused on characteristics of the targets and used a shooter game paradigm in which targets from four ethnic groups were included (Black, Latino, Asian, and White targets). Their results indicated that among non-experts (Study 1) only black targets elicited a shooter bias, as evidenced in response times, while both Black and Latino targets increased the accuracy of decisions to shoot compared to White and Asian targets.

In light of these previous findings, it seems that the next step in establishing the role of threat in producing the shooter bias is to investigate further the threat stereotypically associated with the target outgroup. In all the studies discussed previously, the social categories (either ethnic and/ or religious) to which the targets belonged were clearly visible to the participants and the speed of the shooting responses was ‘‘influenced by negative associations triggered by the visible identity of the target’’ (Unkelbach et al., 2008, p. 1409). Mange et al. (2012) extended this research by introducing a variation of the shooter bias paradigm, which allowed exploration of the effect of social Social Psychology 2016; Vol. 47(1):29–37

category priming independently of the visible characteristics of the targets. They demonstrated that activating social categories such as ‘‘Arab’’ or ‘‘Muslim’’ prior to the videogame provoked a shooter bias toward targets whose group membership was ambiguous (i.e., had no visible cue of their group membership). The mere priming of these outgroups, compared to no activation, was sufficient to facilitate aggressive responses, even if the targets themselves did not necessarily belong to the primed groups. Yet, in the study by Mange et al. (2012), as in the case of most previous shooter game studies, the outgroups toward which aggressive responses were assessed was stereotypically perceived as threatening. Once again, the variable ‘‘outgroup’’ was confounded with threat priming.

Hence, relying both on Sadler et al. (2012) and Mange et al. (2012), the present research sought to determine whether the outgroup must be threatening for its priming to elicit aggressive responses in a shooter paradigm with ambiguous targets, or whether any outgroup priming would elicit similar responses. Hypothesizing a similar process for visible cues of target category (Correll et al., 2011; Miller et al., 2012; Sadler et al., 2012) and prior priming of the category, we expected that only the priming of outgroups stereotypically associated with threat would elicit aggressive responses to ambiguous targets, which would be reflected in an increased shooter bias.

The Present Research The main purpose of this research is to establish that the mere priming of an outgroup is not sufficient to elicit aggressive responses to ambiguous targets through a shooter bias. Rather, we hypothesize that an increased shooter bias would be systematically observed only when the primed outgroup is associated with threat. In order to address this issue, we first conducted a pilot study to identify outgroups stereotypically associated versus not associated with threat. Next, the main study included a manipulation of target group accessibility – ingroup versus non-threatening outgroup versus threatening outgroup. Following Higgins, Rholes, and Jones (1977) and studies dealing with social categories primes (e.g., Bargh et al., 1996), target group accessibility was manipulated between conditions. Following exposure to primes of one category, the participants in all conditions played a shooter game (Mange et al., 2012) in which the targets were males and females with ambiguous ethnicity and religion.

Pilot Study The pilot study aimed to identify ethnic outgroups associated or not associated with threat in our participants’ population. Because the main study used targets with ambiguous ethnicity, a methodological constraint was that to select outgroups whose stereotypical physical appearance was similar to the appearance of target persons in the videogame (i.e., dark hair and dark eyes). In line with this Ó 2015 Hogrefe Publishing

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objective, the perceived threat of Arab, Spanish, and Italian persons was tested among French participants.

To better understand the perceived threat from the three outgroups presented, in reference to Riek et al.’s (2006) meta-analysis, we relied on Integrated Threat Theory (ITT; Stephan & Stephan, 1996, 2000). ITT distinguishes realistic threat from symbolic threat and intergroup anxiety.1 Realistic threats include threat to ‘‘the very existence of the ingroup (e.g., through warfare), threats to the political and economic power of the ingroup, and threats to the physical or material well-being of the ingroup (e.g., their health)’’ (Stephan et al., 2002, p. 1243). Symbolic threat involves ‘‘perceived group differences in morals, values, standards, beliefs, and attitudes’’ (Stephan et al., 2002, p. 1243).

Finally, intergroup anxiety refers ‘‘to feelings of threat people experience during intergroup interactions because people are concerned about negative outcomes for the self, such as being embarrassed, rejected, or ridiculed’’ (Stephan et al., 2002, p. 1243). We assessed the perceptions of realistic threat, symbolic threat, and intergroup anxiety toward different groups among French participants in order to identify outgroups perceived as threatening versus nonthreatening in this population.

Method Participants and Procedure Forty-five French undergraduate students (15 men and 30 women; Mage = 30.38, SDage = 13.89) participated in this study.2 Participants were randomly exposed to one out of three versions of the questionnaire, which differed according to the target group: Arab people (n = 15), Spanish people (n = 15), or Italian people (n = 15). Participants completed the questionnaire alone in a quiet environment.

They were instructed to complete the questionnaire as honestly as possible. Finally, the participants filled out several suspicion checks and demographics questions, and were thanked and debriefed.

Measures Items referring to realistic threat, symbolic threat, and intergroup anxiety were all adapted from Stephan, Ybarra, Martínez, Schwarzwald, and Tur-Kaspa (1998). Participants responded to all items using a Likert-type scale ranging from 1 = not at all to 10 = totally/extremely.

Realistic Threat Twelve items were used, focusing on political (e.g., ‘‘Arab/ Spanish/Italian people dominate French politics more than

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they should’’), economic (e.g., ‘‘Arab/Spanish/Italian people have more economic power than they deserve in this country’’), and security (e.g., ‘‘Insecurity is mostly due to Arab/Spanish/Italian people’’) threats. A score was computed on the basis of these 12 items (a = .97).

Symbolic Threat Twelve items were used, measuring the perceived differences between French people and members of each outgroup in terms of values and worldviews (e.g., ‘‘Arab/ Spanish/Italian people don’t understand the way French people view the world,’’ or ‘‘Arab/Spanish/Italian people should not try to impose their values on French people’’).

A score was computed on the basis of these 12 items (a = .92).

Intergroup Anxiety Participants were instructed to rate the extent to which they experience different feelings when they interact with Arab/ Spanish/Italian people. The feelings rated were nervous, friendly (reverse scored ), uncertain, comfortable (reverse scored ), worried, trusting (reverse scored ), threatened, confident (reverse scored ), awkward, safe (reverse scored ), anxious, and at ease (reverse scored ). A score was computed on the basis of these 12 adjectives (a = .90).

Results and Discussion Dependent measures were analyzed using Multivariate Analysis of Variance (MANOVA) with outgroup target as a between-subject variable. Significant effects of outgroup target emerged on realistic threat, F(2, 42) = 9.77, p < .01, g2p = .32, symbolic threat, F(2, 42) = 9.45, p < .01, g2p = .31, and intergroup anxiety, F(2, 42) = 4.76, p < .02, g2p = .19. On all dimensions, the Arab group was perceived as the most threatening outgroup and Spanish group as the least threatening (Least Significant Difference, LSD tests, all ps < .01). The evaluations of the Italian outgroup were in between the others. Whereas Italians did not differ from the Spanish on realistic threat (LSD test, p = .47) and on intergroup anxiety (LSD test, p = .72), they were perceived as more threatening than Spanish people on the symbolic threat dimension (LSD test, p < .03). All details are presented in Table 1.

The results revealed that Arab people were perceived as the most threatening outgroup, while Spanish people were perceived as the least threatening outgroup on all dimensions of threat among French participants. Accordingly, we decided to use Arab people and Spanish people as the groups to be primed in our main study.

Integrated Threat Theory originally considered negative stereotypes as another category of threat, but later theorizing suggested that stereotypes are more likely an antecedent of threat (Stephan et al., 2002).

Because participants’ gender did not moderate any of the effects we report (all Fs < 1), we will not discuss this variable.

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Table 1. Target outgroup effect on perception of threat Threat dimension

Arab people

Spanish people

Italian people

Realistic threat Symbolic threat Intergroup anxiety

3.60 (2.52) 4.92 (2.27) 4.18 (1.76)

1.29 (0.48) 2.42 (0.92) 2.79 (1.13)

1.69 (1.81) 3.78 (1.22) 2.97 (1.01)

Main Study The main study aimed to demonstrate that an association of the primed outgroup with threat is necessary in order to elicit aggressive responses in the shooter paradigm. The study included a manipulation of target group accessibility and a shooter game. Following exposure to primes of the one group category, the participants in all conditions played a shooter game (Mange et al., 2012) in which the targets were males and females with ambiguous ethnicity and religion.

Increased aggressive responses were expected only after priming an outgroup whose stereotype includes a threatening dimension (compared to nonthreatening outgroup and ingroup primes). Aggressive responses were measured through reaction times and shooter bias reflected in Signal Detection Theory (SDT) indicator c (Stanislaw & Todorov, 1999). Specifically, primes of an outgroup perceived as threatening were expected to elicit faster decisions to shoot when armed and/or lower decisions to not shoot (illustrated by difference in reaction times between gun and no-gun trials), and higher shooter bias (reflected in SDT indicator c) than primes of both a nonthreatening outgroup and the ingroup.

To complement the investigation of aggressive responses, we explored the potential effect different outgroup and ingroup primes on sensitivity (SDT indicator d0 ; Stanislaw & Todorov, 1999), that is, the ability of participants to distinguish between ambiguous targets holding guns and similar targets without guns. This ability is estimated by taking into consideration correct (defined as ‘‘hits’’) and incorrect (defined as ‘‘false alarms’’) ‘‘shoot’’ decisions. Sadler et al. (2012) demonstrated that sensitivity was greater for Black and Latino targets compared to White and Asian targets, suggesting greater sensitivity in response to targets belonging to outgroups associated with threat.

Accordingly, we explored whether threatening outgroup primes would generate greater sensitivity (SDT indicator d0 ; Stanislaw & Todorov, 1999) than nonthreatening outgroup and ingroup primes.

Method Participants Fifty-five French students (24 men, 31 women; Mage = 22.71, SDage = 5.39) participated in this experiment.3 3 4

Participants were randomly assigned to one of three priming conditions: French (n = 15), Arab (n = 20), or Spanish (n = 20). All participants identified themselves as White French people.

Material and Procedure In the first part of the experiment the participants were told that they would complete a test of their French abilities, which actually served as a group priming procedure. Supraliminal priming by a ‘‘scrambled sentences’’ task (Bargh et al., 1996; Chartrand & Bargh, 1996) was used to prime the ‘‘French’’ versus ‘‘Arab’’ versus ‘‘Spanish’’ categories.

Participants had to construct a correct grammatical fourword sentence out of a set of five words suggested (e.g., proposition: watches recalls he occasionally people; correct answer: he occasionally watches people). In each condition, 16 word sets were presented to participants in a random order. In each group priming condition, eight of the sets contained words associated with the target category: French (cooking, Paris, wine, baguette, beret, cheese, chauvinistic, republic), Arab (belly dancing, Scheherazade, camel, Aladdin, calligraphy, couscous, Egypt, sun), or Spanish (sun, warm, flamenco, paella, holidays, bull, Barcelona, sea).

The words associated with each category were selected on the basis of a pretest, in which 98 participants (30 men, 68 women; Mage = 24.09; SDage = 11.07) were asked to specify words that came to their mind when thinking about ‘‘French,’’ ‘‘Arab,’’ and ‘‘Spanish’’ people.4 A computerized lexical association program (Lexico 3, University La Sorbonne – France) was used to identify words statistically associated with each category ( p < .05). Similarly to Mange et al. (2012), the other word sets in all priming conditions were taken from Bargh et al. (1996).

In the second phase, the participants played a shooter game identical to the one used by Mange et al. (2012).

The targets were black and white photographs of eight men and eight women with an ambiguous ethnicity (dark hair, dark eyes). We conducted a pretest in order to ascertain that the ethnicity of the target persons was ambiguous and they were not clearly perceived as being members of any of the primed categories. In order to do so, we presented the photographs to 45 participants (4 male, 40 female, 1 did not specify gender; Mage = 18.89; SDage = 1.20). Each photograph was followed by an open question regarding the ethnicity of the person shown, resulting in 720 spontaneous identifications. Results indicated that the targets were perceived as French in 19.31% of the cases, as Arab in 18.75% of cases, as Spanish in 11.67% of cases, as Romanian in 10.83% of cases, as African in 7.78% of cases, as Italian in 6.95% of cases, and as Greek in 5% of situations. We thus conclude that the targets could not be identified unequivocally as members of one of our primed groups and were therefore ambiguous. Each photograph was paired with an upraised

Participant gender did not moderate any of the effects we report.

In reference to Mange et al. (2012), the category ‘‘Muslim’’ was also added in order to disentangle the ethnic part from the religious dimension linked to Arab people.

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hand holding a black or silver gun, or a similar sized innocuous object (black bottle or silver mug), resulting in 64 target images. These targets were embedded in a picture of a building with four windows (see Figure 1 in Mange et al., 2012). In each trial, a computer program (DirectRT and Medialab – Jarvis, 2006a, 2006b) randomly presented one of the target images in one of the windows. The participants’ task was to press the ‘‘/’’ key on the keyboard, labeled ‘‘shoot,’’ when an armed target appeared and the ‘‘x’’ key, labeled ‘‘don’t shoot,’’ when an unarmed target appeared. The computer program measured their response times. Following Correll et al. (2002), participants were instructed to make a decision as quickly as possible. We allowed a time window of 850 ms for a response. Even if this time window does not favor variability in errors, it does not preclude the analysis of errors that do occur (see Sadler et al., 2012 for an example) and allows analysis of reaction times. A warning appeared whenever a participant was too slow and/or made an incorrect decision. The game began with six training trials with targets randomly chosen by the computer. The actual test phase consisted of 64 trials.

After completing the shooter game, the participants filled out several suspicion checks and a demographics questionnaire, and were then thanked and debriefed.

Measures The shooter game paradigm is an interesting method of assessing aggressive responses because of the different ways in which responses can be analyzed. First, reaction times can be assessed (e.g., Correll et al., 2002 or Mange et al., 2012). In this procedure, only correct answers are processed and dangerousness and decision are taken into account. Reaction times contain information about aggressive responses (differences between reaction times to armed targets and unarmed targets as a function of target). Second, responses can be analyzed on the basis of SDT indicators (Stanislaw & Todorov, 1999). This last method (e.g., Correll, Park, Judd, Wittenbrink, Sadler, et al., 2007 or Unkelbach et al., 2008) relies exclusively on the analysis of the shoot decisions which are considered as ‘‘hits’’ if the decision is correct (i.e., shooting an armed target) and as ‘‘false alarms’’ if the decision is incorrect (i.e., shooting an unarmed target). This analysis yields two parameters.

A shooter bias can be identified through SDT indicators such as b or c,5 which reflect aggressive responses. In addition, sensitivity, that is, the ability to distinguish a gun from an innocuous object, can be measured through SDT indicator d0 . We believe that a systematic approach encompassing these indicators will allow us to arrive at a more comprehensive and precise understanding of the relationship between group priming, perceived threat, and aggressive responses (see Correll et al., 2011 for an example of systematic approach).

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Table 2. Mean (and standard deviations) for differences in reaction times for gun and no-gun trials, c and d0 as a function of group priming condition and target gender French priming Differences in reaction times Male 45.77 (39.27) Female 10.76 (34.16) c Male 0.12 (0.27) Female 0.08 (0.27) d0 Male 1.32* (0.89) Female 1.05* (0.78)

Arab priming

Spanish priming

between gun and no-gun trials 67.23 (37.74) 20.98 (42.15) 61.73 (40.10) 14.83 (38.93) 0.25* (0.27) 0.20* (0.24)

0.01 (0.31) 0.03 (0.33)

2.48* (0.64) 2.24* (0.58)

2.01* (1.07) 1.83* (0.86)

Note. *Indicates that the mean is significantly different from zero.

Results Difference in Reaction Times Between Gun and No-Gun Trials In keeping with Correll et al. (2002), all trials in which participants had timed-out (reaction times greater than 850 ms) were excluded from the data. All trials in which participants made an incorrect response (shooting an unarmed target or not to shoot an armed target) were also excluded from the data. This resulted in the exclusion of data from 3.13% of the trials across participants with a maximum of 9.38% of the trials for any one participant. Differences in response latencies between gun and no-gun trials on the remaining trials were entered into a mixed-model ANOVA, with group priming condition (French vs. Arab vs. Spanish) as a between-subject factor and target gender (male vs. female) as a repeated factor. The resulting cell means converted back to millisecond metric are presented in Table 2 (raw data of the Main Study are provided in ESM 1).

As expected, a main effect of group priming was observed on differences in reaction times between gun and no-gun trials, F(2, 52) = 12.83, p < .01, g2p = .33.

To identify the source of the effect, we conducted two planned contrasts. First, we compared the ingroup to both outgroup priming conditions (French = 2, Arab = +1, Spanish = +1). This contrast was not significant ( p = .16), indicating that the distinction ingroup versus outgroups do not explain the observed main effect.

Next, we compared the threatening to the nonthreatening outgroup priming condition (French = 0, Arab = +1, Spanish = 1). This contrast was significant (p < .01), indicating that the difference in reaction times between gun and no-gun trials was significantly different between Spanish and Arab outgroup primes. Specifically,

As underlined by Stanislaw and Todorov (1999), whereas historically the response bias has been measured by the indicator b based on a likelihood ratio, authors (e.g., Snodgrass & Corwin, 1988) now recommend to use the indicator c directly based on the decision variable and not affected by changes in d0 .

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the threatening outgroup prime elicited higher differences between gun and no-gun trials compared to a nonthreatening outgroup prime. To go into depth in this effect, post hoc tests were conducted. These complementary analyses revealed that differences between gun and no-gun trials were more important in Arab condition (M = 64.48, SD = 6.77) compared to Spanish condition (M = 17.91, SD = 6.77; LSD test, p < .01)6 but also to French priming condition (M = 28.26, SD = 7.82; LSD test, p < .01).

Interestingly, French priming condition did not differ significantly from Spanish condition (LSD test, p = .32).

Besides not moderating the main effect of group priming and in keeping with previous research (e.g., Plant et al., 2011), we found a significant effect of target gender, F(1, 52) = 5.41; p < .05; g2p = .09, on this measure. Specifically, difference in reaction times between gun and no-gun trials was higher for male targets (M = 45.56, SD = 43.85) than for female targets (M = 30.78, SD = 44.29).

SDT Index c and d0 Indicators c and d0 were computed considering shooting at an armed target as a ‘‘hit’’ and shooting at an unarmed target as a ‘‘false alarm.’’ A negative value of c indicates a bias to ‘‘shoot’’ whereas a positive value indicates a bias to ‘‘not shoot.’’ On the d0 indicator, a value of 0 indicates an inability to distinguish guns from innocuous objects, and the higher the value, the greater the ability to distinguish between them.

The c and d0 7 scores were entered into a mixed-model MANOVA, with group priming condition (French vs. Arab vs.

Spanish) as a between-subject factor and target gender (male vs. female) as a repeated factor. The detailed means and standard deviations are presented in Table 2.

As assumed, a main effect of group priming condition on indicator c was observed and confirmed the results based on difference in reaction times, F(2, 52) = 6.298, p < .01, g2p = .21. To decompose this effect, we again tested the same planned contrasts described earlier. The contrast comparing the ingroup to the outgroup priming conditions was not significant. However, the contrast comparing the threatening versus nonthreatening outgroup conditions was significant ( p < .01), demonstrating that participants presented a bias after a threatening but not after a nonthreatening outgroup prime. A comparison of each c score for each group prime condition to zero score confirmed that c score differed significantly from 0 only in the Arab group priming condition (male targets: t(19) = 4.14, p < .01; female targets: t(19) = 3.84, p < .01). Finally, planned contrasts integrating also the target gender (coded 1, +1 respectively associated to male and female targets) revealed no significant effects (all ps < .10).

Besides not moderating the main effect of group priming, a marginal effect of target gender was also observed on indicator c, F(1, 52) = 3.49, p = .07, g2p = .06, revealing a

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tendency to a greater bias toward shooting men (M = 0.12, SD = 0.04; significantly different from zero, t(54) = 2,95, p < .01) than toward shooting women (M = 0.03, SD = 0.04; not significantly different from zero, t(54) = 0.99, p = .32).

Regarding indicator d0, the main effect of group priming on indicator d0 was also significant, F(1, 50) = 9.54, p < .01, g2p = .28. We computed the same planned contrasts described previously. Interestingly, only the contrast comparing ingroup priming to outgroup priming was significant ( p < .01) revealing that while d0 significantly differed from zero in all conditions (all ps < .01), it was significantly lower after an ingroup prime (M = 1.19, SD = 0.21) than after an outgroup prime. The contrast comparing the threatening to the nonthreatening outgroup priming conditions was only marginally significant ( p = .09), suggesting that d0 after the Spanish group prime was somewhat lower than after the Arab group prime. Finally, planned contrasts integrating also the target gender (coded 1, +1, respectively associated to male and female target) revealed no significant effects (all ps < .10). Besides not moderating the main effect of group priming, an effect of target gender was observed, F(1, 50) = 6.56, p < .05, g2p = .12. Male targets (M = 2.02, SD = 0.98; significantly different from zero, t(52) = 15.02, p < .01) generated higher sensitivity than female targets (M = 1.679, SD = 0.86; significantly different from zero, t(52) = 15.08, p < .01).

Discussion This research aimed to understand the intergroup processes underlying the effects of category priming on the shooter bias by manipulating the threat dimension associated with the primed groups. We replicated the findings of Mange et al. (2012), demonstrating that the mere priming of the Arab outgroup leads to a shooter bias toward targets whose category membership is ambiguous. These finding with a French sample are similar to those obtained by Mange et al. (2012) with an American sample. Moreover, in the present study we were able to show that only the priming of the Arab group, which is stereotypically associated with threat, generated the effect. The results were consistent across indicators of reaction times and bias indicator c. Interestingly, d0 indicator revealed that both outgroup primes (whether associated with threat or not) significantly increased the ability to distinguish between a gun and an innocuous object compared to an ingroup prime. This effect tended to be stronger for the Arab outgroup prime compared to the Spanish outgroup prime. Hence, these results indicate that (1) an outgroup must be stereotypically associated with threat for its priming to increase aggressive responses; and (2) various outgroup stimuli, whether threatening or not, appear to instigate a need for careful consideration, therefore increasing the importance of distinguishing dangerous tools such as guns from innocuous tools.

This information was already given by the contrasts described above.

Two participants presenting a negative d0 scores were excluded from the analysis.

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Our findings demonstrate that increased aggressive responses in the shooter paradigm after priming of a threatening outgroup (vs. ingroup) are not merely a product of ingroup favoritism. These results affirm the distinction, made in previous research, between ingroup favoritism and outgroup derogation (Brewer, 1999). Although ingroup favoritism is quite ubiquitous, specific conditions are required for intergroup aggression to emerge (Brewer, 2007). Moreover, threat is an important factor in eliciting intergroup hostility (Riek et al., 2006). Consistent with these notions, our findings show that priming a nonthreatening outgroup did not elicit more aggressive responses than ingroup priming, but priming a threatening outgroup did increase aggressive responses.

The effects of temporary accessibility of constructs on subsequent behaviors have been studied extensively (see review in Higgins, 2011) and have been demonstrated with regard to judgments (Devine, 1989), recognition of objects (e.g., Eberhardt, Goff, Purdie, & Davies, 2004; Payne, 2001), personal attitudes (Kawakami, Dovidio, & Dijksterhuis, 2003), and behaviors (e.g., Bargh et al., 1996, Study 2). Research has also established that members of out-groups perceived as threatening (e.g., African Americans) elicit negative reactions (e.g., Devine & Elliot, 1995; Ford, 1997; Schmidt & Nosek, 2010). These new results complement and support previous results regarding the effect of social category priming on aggressive responses toward a computer (African-American outgroup priming; Bargh et al., 1996, Study 3; Cesario et al., 2010), toward ingroup targets during an interaction (African-American outgroup priming; Chen & Bargh, 1997), and toward ambiguous targets (Arab vs. Muslim outgroup priming; Mange et al., 2012). It should be noted that none of these effects require that the target of the aggressive behavior be identified as a member of the primed outgroup. Our findings are consistent with the notion that the mere priming of a threatening outgroup can affect responses even toward targets that are not necessarily related to the prime.

Although our findings demonstrate the necessity of threat in increasing aggressive responses when an outgroup is primed, they do not allow us to distinguish the effects of the different dimensions of threat, which were assessed in a separate pilot study. It is possible that different dimensions of threat are differentially related to aggressive responses.

Previous studies that examined the effects of different dimensions of threat on intergroup attitudes or aggressive behavioral intentions have yielded inconclusive findings.

Some reveal a stronger role of realistic (vs. symbolic) threat in the process (e.g., Stephan et al., 2002 for white participants) and others a stronger role of symbolic threat (e.g., Velasco González, Verkuyten, Weesie, & Poppe, 2008).

Overall, studies suggest that both types of threat are related to negative attitudes toward outgroups (see Riek et al., 2006 for a meta-analysis). As underlined by Riek et al. (2006), although all dimensions of threat may result in negative attitudes toward outgroups, different dimensions may lead to different behavioral outcomes. Hence, including measures of the nature of the threat in future studies could give a more precise understanding of the underlying process of intergroup aggression on the behavioral side. Ó 2015 Hogrefe Publishing

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Our findings also reveal an increase in the ability of participants to distinguish between dangerous tools such as guns and innocuous tools after outgroup priming, whether the primed outgroup was threatening or not. What can we deduce from this increase and what does it represent?

One possibility is that outgroups have a potential to be threatening, even if this potential does not always materialize. Hence, when an outgroup stimulus is present, attention and scrutiny are required in order to determine whether the outgroup constitutes a threat. This need to determine whether the outgroup constitutes a threat may have led to the development of an automatic tendency to increase vigilance when an outgroup stimulus is present which could subsequently increase the ability to distinguish between dangerous and innocuous stimuli. As no measure of vigilance was included in our research, no conclusion can be drawn on this point. However, research indicates that a tendency to increase vigilance in the presence of an outgroup can be found even among nonhuman species (Mahajan et al., 2011), indicating that it may be an adaptive response from an evolutionary perspective. Further, we may hypothesize that if increased vigilance leads to the conclusion that the outgroup constitutes a threat with high certainty, then vigilance could give rise to aggressive responses. This possibility is suggested by the findings showing that beyond the general increase in the ability to distinguish between dangerous and innocuous objects following outgroup priming, the threatening outgroup primes elicited even greater distinctive ability than the nonthreatening outgroup primes.

Hence, if the increased distinctive ability is due to vigilance in response to outgroup primes, it could be considered as a first step toward potential outgroup derogation. One could imagine a sort of threshold in threat perception which, when reached and confirmed by various indicators of potential danger, may activate aggressive responses. Unfortunately, the literature on the shooter bias has rarely considered the issue of vigilance and its indicators. This limits our ability to interpret previous results in light of our reasoning on vigilance. In order to expand on our preliminary results and explore the issue of vigilance more systematically, future research may need to incorporate indicators of vigilance into studies using the shooter paradigm as well as other methodologies. Another possible interpretation of the increase in d0 would be to consider it as an increase of accuracy in information processing. This second interpretation would suggest that people process information more superficially when primed with ingroup compared to outgroups, which may activate a more systematic scrutiny of the environment. However, both of these interpretations of the increase in d0 after outgroup priming in our study, whether as an indicator of vigilance and/or of accuracy motivation – are not entirely consistent with one of the results of Sadler et al. (2012). Sadler et al.

(2012) found that Asian targets elicited the same value of d0 as White and that these d0 s were lower than for LatinoAmericans and Afro-American targets. However, the participants in Sadler et al.’s study belonged to diverse ethnic groups, and therefore the status of the targets as ingroup or outgroup members was inconsistent across participants.

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of ingroup versus outgroup targets from their findings.

Nonetheless, the combination of our findings with those of Sadler et al. (2012) suggests that factors other than threat may affect the ability to distinguish between guns and innocuous objects. One possibility is that other dimensions of stereotypes play a role in this effect. Future research could further clarify the issue.

Conclusion The present study expands on previous research with the shooter paradigm by comparing the aggressive reactions that follow the priming of two different outgroups with distinct threat characteristics and by considering various indicators.

This is the first replication of the ‘‘mere priming effect’’demonstrated by Mange et al. (2012) on aggressive responses.

Indeed, the mere priming of the threatening outgroup led to a shooter bias toward targets whose category membership is ambiguous. Importantly, the effect was observed only after the priming of the outgroup stereotypically associated with threat and not a nonthreatening outgroup. In addition to complementing previous studies regarding the effect of group priming studies on aggressive responses (e.g., Bargh et al., 1996, Study 3; Chen & Bargh, 1997; Cesario et al., 2010), the present research explored more precisely the role of group characteristics and intergroup relations in driving the shooter bias. From a social and civil perspective, it is reassuring to observe that although reminders of outgroups increase ability to distinguish between dangerous and innocuous stimuli, they do not automatically instigate aggressive responses. At the same time, the facts that any outgroup primes may be associated with a perceived potential threat (as indicated by increased ability to distinguish between dangerous and innocuous objects), that priming threatening outgroups can increase aggressive responses, and that all of this can happen even when the targets are ambiguous and not necessarily outgroup members, may be causes for social concern.

Electronic Supplementary Material The electronic supplementary material is available with the online version of the article at http://dx.doi.org/10.1027/ 1864-9335/a000255 ESM 1. Raw data (sav file).

Raw data of the Main Study.

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Received July 23, 2014 Revision received May 28, 2015 Accepted July 7, 2015 Published online December 30, 2015

Jessica Mange Psychology Department University of Caen (NIMEC – EA 969) Esplanade de la paix 14 032 Caen Cedex France Tel. +33 2 3156-5840 Fax +33 2 3156-6693 E-mail jessica.mange@unicaen.fr

Social Psychology 2016; Vol. 47(1):29–37

Original Article

The Validity of Crowdsourcing Data in Studying Anger and Aggressive Behavior A Comparison of Online and Laboratory Data Johannes Lutz University of Potsdam, Germany Abstract. Crowdsourcing platforms provide an affordable approach for recruiting large and diverse samples in a short time. Past research has shown that researchers can obtain reliable data from these sources, at least in domains of research that are not affectively involving. The goal of the present study was to test if crowdsourcing platforms can also be used to conduct experiments that incorporate the induction of aversive affective states. First, a laboratory experiment with German university students was conducted in which a frustrating task induced anger and aggressive behavior. This experiment was then replicated online using five crowdsourcing samples. The results suggest that participants in the online samples reacted very similarly to the anger manipulation as participants in the laboratory experiments. However, effect sizes were smaller in crowdsourcing samples with non-German participants while a crowdsourcing sample with exclusively German participants yielded virtually the same effect size as in the laboratory.

Keywords: crowdsourcing, online research, anger, aggression, frustration, mechanical turk

Crowdsourcing markets like Amazon Mechanical Turk are increasingly used for data collection in psychological research and have become a subject of research themselves.

On these online platforms, users (‘‘requesters’’) can hire other users (‘‘workers’’) to work on computerized tasks in exchange for monetary compensation. Researchers can use crowdsourcing markets to collect large and diverse samples in a very short amount of time for only minimal fees (see Mason & Suri, 2012). Accumulating evidence suggests that data obtained from these sources is sufficiently reliable and highly similar to data acquired from conventional samples (Buhrmester, Kwang, & Gosling, 2011; Casler, Bickel, & Hackett, 2013; Paolacci & Chandler, 2014). Crowdsourcing samples have been used successfully to replicate established findings from various fields of psychological science, mostly in the domain of judgment and decision making (Goodman, Cryder, & Cheema, 2013; Horton, Rand, & Zeckhauser, 2011; Paolacci, Chandler, & Ipeirotis, 2010) but also in studies that go beyond simple survey-type designs, for example, by employing response time measures (Simcox & Fiez, 2014), diary studies (Boynton & Richman, 2014), or bogus partner interactions (Summerville & Chartier, 2013).

Further, crowdsourcing samples have been used in recent correlational and experimental studies from personality, social, and clinical psychology to test hypotheses regarding a broad range of topics, such as attitudes toward mental Social Psychology 2016; Vol. 47(1):38–51 DOI: 10.1027/1864-9335/a000256

illness (Bizer, Hart, & Jekogian, 2012), processes underlying skepticism (Campbell & Kay, 2014), need-thwarting in interpersonal relationships (Costa, Ntoumanis, & Bartholomew, 2015), shame and self-change (Lickel, Kushlev, Savalei, Matta, & Schmader, 2014), dark triad traits and vocational interests (Jonason, Wee, Li, & Jackson, 2014), and non-suicidal self-injury disorder (Andover, 2014).

Even though these results speak in favor of using crowdsourcing platforms as participant pools in general, it remains unclear if this holds true for every domain of psychological research. Especially studies that take much time, are strenuous, or induce negative affect might not be suitable to be crowdsourced. However, a number of experimental paradigms from different research domains rely on systematically creating aversive affective situations.

To study models of self-regulation, fatiguing experimental procedures are often used to manipulate participants’ levels of ego-depletion (Baumeister, Bratslavsky, Muraven, & Tice, 1998). In research on mortality salience, death-related cognitions, and emotions like anxiety are often experimentally induced (Routledge et al., 2010). Ego depletion and mortality salience paradigms have already been used successfully in crowdsourcing samples (Burns, Hart, Kramer, & Burns, 2014; Chopik & Edelstein, 2014; Chow & Lau, 2015), but none of the experimental manipulations used in these studies significantly induced negative affective Ó 2015 Hogrefe Publishing

J. Lutz: Crowdsourcing Data in Studying Anger and Aggression

states. In experiments on ostracism, negative feelings are often evoked by making participants feel socially excluded (Williams & Nida, 2011). There is some first evidence that ostracism paradigms like ‘‘Cyberball’’ can also be employed in crowdsourcing samples (Wolf et al., 2015).

Further, studies in which sadness (Rick, Pereira, & Burson, 2014) or low social status (Davis & Reyna, 2015) were experimentally induced suggest that crowdsourcing platforms may also be used to collect data of good quality in fields of research that rely on affectively involving or even slightly aversive paradigms. However, studies that have explicitly tested the validity of crowdsourcing data in such research domains as well as systematic comparisons with laboratory data are lacking.

Another prominent domain in which it is sometimes necessary to put participants in aversive situations is research on aggressive behavior. To study antecedents, processes, and consequences of aggressive affect, cognition, and behavior, experimental procedures are used that provoke or frustrate participants to elicit aggressive response tendencies. One often-used manipulation to provoke participants is the essay-evaluation paradigm (e.g., Krahé & Bieneck, 2012). Participants are asked to write an essay on a generic topic which is ostensibly evaluated by another participant afterwards. In the provocation condition, participants receive negative bogus feedback, whereas feedback for subjects in the control group is neutral or positive.

Another frequently-used approach for evoking aggressive tendencies in the laboratory is to induce negative affect through the experience of frustration (Berkowitz, 1989), for instance by having participants work on unsolvable puzzles (Geen, 1968).

Most studies regarding the suitability of data collection via crowdsourcing platforms have employed affectively neutral or at least not very emotionally involving experimental manipulations (e.g., Paolacci et al., 2010). The present study was conducted to explore the validity of data from participants recruited through crowdsourcing in an experiment on aggressive behavior which comprised the induction of aversive affective states.

Since crowdsourcing workers are used to complete dozens of short tasks by the hour and may follow a ‘‘time is money’’-rationale, they may not be attentive enough to affectively engage with experimental tasks. Evidence concerning crowdsourcing participants’ attentiveness is mixed.

While some studies report crowdsourcing participants to be less attentive (Goodman et al., 2013, study 2) and distracted by other tasks (Chandler, Mueller, & Paolacci, 2014), other studies found no difference in comparison to college students (Paolacci et al., 2010) or even higher attentiveness in crowdsourcing samples (Hauser & Schwarz, 2015).

Because evidence regarding the issue of attentiveness is mixed and the few studies that looked into the problem did not involve affectively involving experiments, the question still remains if participants from crowdsourcing samples are attentive and conscientious enough for this kind of research. If there was a general problem with attentiveness, it should not be possible to induce a specific affect at all. But even if the induction of affective states is possible in a crowdsourcing context, the experience of aversive Ó 2015 Hogrefe Publishing

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emotions itself can pose a problem for the continuation of the study. Unlike in laboratory settings, participants in an online study can quit the experiment easily at any time.

Therefore, it may be possible that the induction of an aversive state like being frustrated or angry will only lead participants to drop out from the study. And even if they decide to continue with the experiment, they may easily distract themselves from the negative experience by having a break and temporarily switching to another website. If so, the effects of an affectively negative experimental manipulation may simply dissipate. At the same time, research on aggression and other fields which rely on affectively involving or even aversive experimental procedures may benefit significantly from uncovering new sources to access participants pools beyond traditional college samples. Especially paradigms that make use of deception, like the essay-evaluation paradigm, are difficult to employ more than once within the same pool of participants. Even though (non)-naivety is also an issue there (Chandler et al., 2014; Chandler, Paolacci, Peer, Mueller, & Ratliff, 2015), extending participant pools to crowdsourcing markets may enable researchers to recruit more diverse samples, obtain more reliable results through massive replication (Asendorpf et al., 2013), and finally advance faster from theory to experiment and back (Mason & Suri, 2012).

Therefore, the present study was set to test the validity of data acquired through crowdsourcing samples in affectively involving experiments. This was done by comparing data from a laboratory experiment on aggressive behavior with five online replications of the same experiment, which were conducted through three crowdsourcing markets.

Overview of Studies An experiment was designed to elicit anger affect and aggressive behavior by means of a situational manipulation.

Using the General Aggression Model (DeWall & Anderson, 2011) as a theoretical framework, it was hypothesized that in comparison to a control condition, the experience of frustration would lead participants to experience (1) more anger affect, (2) less positive affect, and (3) increased arousal.

Further, it was expected that frustrated participants would act (4) more aggressively and (5) less prosocially than non-frustrated ones (Berkowitz, 1989).

After establishing the expected effects in the laboratory, the main part of the study was set to test if it would be possible to conduct a series of successful replications of the same experiment using crowdsourcing participant pools.

To test the equivalence of online and laboratory data, five crowdsourcing samples were collected and the same tests were performed as on the laboratory data and the effect sizes were compared. Further, sample characteristics and participants’ survey behavior were compared between laboratory and online samples as well as within the online samples. Three samples were collected via Amazon Mechanical Turk (AMT), which is currently the crowdsourcing platform most often used in psychological research. Since findings from one crowdsourcing platform must not necessarily translate to another, an additional sample was acquired Social Psychology 2016; Vol. 47(1):38–51

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J. Lutz: Crowdsourcing Data in Studying Anger and Aggression

Table 1. Sample characteristics Sample

N

Gender

Age M (SD)

Country

Compensation

Laboratory

126

68 men 57 women

22.4 (3.7)

Germany

Course credit

AMT Masters

58

25 men 33 women

36.8 (11.1)

USA

$0.25

AMT Restricted

125

54 men 71 women

36.3 (12.9)

USA

$0.25

AMT Non-restricted

129

59 men 70 women

35.0 (11.1)

USA (58%) India (34%) Other (8%)

$0.25

Microworkers

141

82 men 59 women

32.4 (10.2)

USA (68%) UK (16%) Canada (11%) Australia (4%) Other (1%)

$1.75

Clickworker

146

69 men 77 women

38.2 (12.7)

Germany

€2

Note. Ns = valid responses excluding dropouts.

via Microworkers, an alternative crowdsourcing platform (Hirth, Hoßfeld, & Tran-Gia, 2011). Because neither AMT nor Microworkers offer access to a substantial number of German participants, an exclusively German crowdsourcing sample was collected through a rather new platform called Clickworker to control for potential confounding of method of data collection and nationality.

Amazon Mechanical Turk allows requesters to preselect potential participants based on the quantity and quality of their prior performance in the market. The system keeps track of the number of tasks a worker has ever opted in for as well as his or her rate of approval by requesters. This provides researchers with means to choose only participants that have already proven to be reliable and thereby possibly enhance the quality of the gathered data (Peer, Vosgerau, & Acquisti, 2014). To further validate this quality indicator, AMT samples were composed of (a) workers with the highest prior qualification, (b) workers with high qualification as defined in the literature (Peer et al., 2014), or (c) all workers, regardless of prior qualification. The Microworkers and Clickworker platforms do not yet incorporate comparable worker qualification systems.

Results of a pilot study (see below) revealed rather strong effects of the frustration manipulation on measures of affect. However since previous research (Buss, 1963) reported only moderate effects of frustration experiences on aggressive behavior and effect sizes could possibly be smaller in online samples, a priori power analyses were conducted to establish the required Ns for the laboratory and online samples to ensure sufficient power to test for medium effects on the behavioral dependent measure.

1

The required sample size to achieve statistical power of .80 was computed with G*Power 3 (Faul, Erdfelder, Buchner, & Lang, 2009). Assuming a medium effect of f = .25 (g2p = .06), the required sample size for an ANCOVA model with two groups and three covariates was N = 128. Whenever possible, online samples were moderately oversampled to be able to buffer potential loss of power due to response bias or other reasons that might lead to the exclusion of cases.1

Method Participants The laboratory sample consisted of 126 German college students (45% female). Their mean age was 22.4 years (SD = 3.7). The students received course credit in return for their participation. Participants in the online samples (Ns = 58–146, see Table 1 for an overview of sample characteristics) were on average 13.2 years older than those in the laboratory sample. The proportion of male and female individuals in the online samples was similar to the laboratory sample (42–57% female).

Amazon Mechanical Turk samples were chosen to represent the upper and lower limits of available worker qualifications in the AMT market, as well as a manually restricted sample of qualified workers most often used in research (Peer et al., 2014). The AMT Masters sample was entirely made up by highly qualified senior workers,

In case of the AMT Masters sample, it was not possible to collect the required sample size in reasonable time, probably because the compensation was too low for highly qualified AMT users.

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so-called Masters. Masters are elite workers who have demonstrated proficiency and reliability on a large number of different tasks on the AMT marketplace. Participation was further restricted to workers from the United States, which make up the vast majority of Masters. The AMT Restricted sample consisted of workers that were prescreened for manually defined criteria regarding the quantity and quality of their prior performance. To ensure high qualification, only workers who had finished 1,000 tasks or more and with an approval rate of 95% or more were invited to participate. Again, only individuals from the US could take part. The AMT Non-restricted sample was collected without any constraints regarding prior qualification or nationality. In the description of the study and the initial instructions, it was only stressed that English language proficiency was mandatory to successfully finish the task. The majority of participants in this sample identified themselves as US citizens (58%), followed by 34% from India. Participation in the Microworkers study was not restricted in terms of prior qualification but only open for workers from English-speaking countries. Again, the majority of participants reported to be from the United States (68%, see Table 1). All participants sampled through the Clickworker platform identified themselves as German citizens. Previous research has indicated that monetary reimbursement is not the most influential factor motivating participation in crowdsourcing platforms (Buhrmester et al., 2011), and paying more does not necessarily lead to more accuracy (Rogstadius et al., 2011). Therefore, compensation in the online samples was not varied systematically. Instead, participants in the AMT and Microworkers samples were paid a rather low reimbursement considering the length of the task. All participants in the AMT samples received a reimbursement of $0.25. This amount was low, actually close to the minimum hourly wage for which workers can be expected to accept a task (Mason & Suri, 2012).

This strategy was chosen to test if it would be possible to obtain data of acceptable quality even under these restricted circumstances. However, it has to be noted that this compensation cannot be considered fair payment. As long as payment is not part of the experimental design, researchers should generally pay attention to adequately compensate crowdsourcing participants. Information on fair payment and other ethical issues can be found in the ‘‘Guidelines for Academic Requesters’’ published by the AMT worker community ‘‘Dynamo’’ (2014). The minimum wage accepted by Microworkers for a task of this length was $1.75 at the time of the assessment. Since the collection of the Clickworker data was last in line and the results from the AMT and Microworkers samples already indicated good data quality even with very low monetary rewards, it was decided to pay participants in the Clickworker sample a substantially higher compensation. Considering the length of the task, the reimbursement of €2 corresponds to the German hourly minimum wage.

To best ensure participants’ naivety in all samples (Chandler et al., 2014, 2015) the TurkGate script (Goldin & Darlow, 2013) was used to prevent AMT workers from participating in more than one of the conducted experiments. Internal settings of the Microworkers and Ó 2015 Hogrefe Publishing

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Clickworker platforms were used to avoid multiple submissions in the respective experiments.

Procedure Upon their arrival, participants in the laboratory sample were informed that they would take part in a study on attentional control. They were randomly assigned to either the frustration condition or the control group and seated in front of a computer. The whole experiment was run as a browserbased survey, and participants were guided by instructions on the screen. On all crowdsourcing platforms, participants were invited to participate in a psychological study on attentional control. The task description also mentioned that it would contain an anagram puzzle. Further, participants were informed about the expected duration of the task and the reimbursement they would be paid. After accepting the task, participants were redirected to the English version of the same browser-based experiment that was used in the laboratory study.

After requesting general demographic information, affect, and arousal were measured for the first time to establish a baseline. In the next part of the experiment, participants were asked to work on an anagram task (DeJoy, 1985). On every trial, a letter string (e.g., ‘‘DOGO’’) was presented in the middle of the screen and participants had 30 s to reorganize it into an actual word (‘‘GOOD’’).

In the frustration condition, only the first one was easy to solve and the six following anagrams were unsolvable. In the control condition, all anagrams were easy to solve. Subsequently, affect, and arousal were measured for the second time to capture the effect of the frustration manipulation. In the last part of the experiment, participants were asked to help with the continuation of the study by choosing anagrams of varying difficulty levels for a future participant.

This was explained with the ostensible need to control for experimenter effects. In fact, the number of very difficult anagrams selected for the alleged other participant represented the measure of aggressive behavior and the number of easy anagrams an index of prosocial behavior. After that, participants were debriefed and thanked. In the online samples, all participants were approved and paid shortly after they had submitted their responses.

Since it was the last sample to be collected, the survey for the Clickworker sample was modified to better account for cases of dropout which were observed in the other online samples. A ‘‘controlled dropout’’ option was introduced to prevent participants from quitting the experiment without being debriefed. During the whole study, a button labeled ‘‘quit survey and delete all data’’ was presented in the lower right corner of the screen. Clicking this button deleted all previously submitted data and redirected participants to a full debriefing. The debriefing also contained the option to watch a funny video to induce positive affect.

If participants tried to exit the survey by simply closing the browser, a pop-up alert was triggered, asking the participant to use the ‘‘delete all data’’ button to exit the survey.

Further, participants in the Clickworker sample proceeded to an additional positive affect induction procedure and a Social Psychology 2016; Vol. 47(1):38–51

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J. Lutz: Crowdsourcing Data in Studying Anger and Aggression

Table 2. Internal consistencies (Cronbach’s a) Anger T1 Anger T2 Anger T3 STAXI Positive affect T1 Positive affect T2 Positive affect T3

Lab

AMT Masters

AMT Restricted

AMT Non-restricted

Microworkers

Clickworker

.79 .89 X .94 .86 .87 X

.85 .94 X .96 .82 .86 X

.78 .91 X .95 .83 .88 X

.89 .90 X .95 .89 .93 X

.90 .93 X .98 .85 .87 X

.89 .91 .91 .97 .85 .87 .93

Notes. T1 = Pre-manipulation; T2 = Post-manipulation; T3 = Follow-up.

subsequent final assessment of affect after the actual end of the experiment. To induce positive affect, participants were asked to remember a moment in their lives that had made them feel really happy (Martin, 1990). This was done to better ensure that any possible residual negative affect had died down before participants left the survey.

The effectiveness of the anagram frustration manipulation to induce affective precursors of aggressive behavior as well as its appropriateness for online research was pretested in a pilot study (N = 64 German students, 88% female). To be able to use an anger-evoking manipulation in online experiments, the effect of the manipulation should be substantial but at the same time wear off rather fast. That way, meaningful experiments can be conducted without harming participants, even in case of premature dropout.

Participants in the pilot study were presented with the anagram task described above. After the assessment of the dependent affective measures (anger and positive affect), participants took part in an allegedly unrelated study on consumer behavior. The task was to handle and evaluate an office tool (a magnetic board). Actually, this part was introduced to have participants engage in an affectively neutral task before testing the temporal stability of the frustration effects. To do so, affect was measured for a final time right after the product evaluation. The anagram task proved to be effective. Frustrated individuals reported significantly more anger (F[1, 59] = 10.99, p < .01, g2p = .16) and less positive affect (F[1, 59] = 16.74, p < .001, g2p = .22) than participants in the control group.

Even though these effects were quite strong, they proved to be only short lived. After the product evaluation task, which took participants 2 min and 52 s on average (SD = 00:54), no differences between the experimental groups regarding anger (F[1, 59] = 0.71, p = .40, g2p = .01) or positive affect (F[1, 59] = 1.11, p = .29, g2p = .02) remained significant. The results of the pilot study suggest that the anagram task is effective to induce feelings of anger but that these effects vanish in short time.

Measures Anger and Positive Affect Anger and positive affect were measured with adjective lists adapted from Krahé and Bieneck (2012). Positive affect was assessed pre- and post-manipulation with three items Social Psychology 2016; Vol. 47(1):38–51

(‘‘I feel . . . joyful, relaxed, happy’’) employing a 9-point scale (1 ‘‘not at all’’ – 9 ‘‘very much’’). Anger was measured pre- and post-manipulation using the same format (‘‘I feel . . . upset, irritable, angry’’). To also include a psychometrically established instrument for the focal dependent variable, anger was additionally measured post-manipulation with the STAXI state anger scale (Spielberger, Sydeman, Owen, & Marsh, 1999). Responses on this measure were also made on a 9-point scale (1 ‘‘not at all’’ – 9 ‘‘very much’’). Subjectively perceived level of arousal was measured with a 9-point version (1 ‘‘calm’’ – 9 ‘‘excited’’) of the Self-Assessment Manikin (Bradley & Lang, 1994). No further measures were collected. Internal consistencies for all measures in all samples proved satisfactory (as = .78–.98, see Table 2).

Aggressive and Prosocial Behavior A variation of the Tangram Task (Gentile et al., 2009; Saleem, Anderson, & Barlett, 2015; Saleem, Anderson, & Gentile, 2012) was used to measure aggressive behavior as well as helping behavior. Participants were asked to choose the difficulty level of anagrams that would ostensibly be assigned to future participants. They were provided with a list of 20 anagrams which were explicitly labeled as being easy, medium, difficult, or very difficult (five each) and asked to mark seven of them to be assigned to another participant. The number of very difficult anagrams chosen was used as an index of the strength of aggressive behavior and the number of easy anagrams as a measure of prosocial behavior. The tangram task is a well-validated measure of aggressive and prosocial behavior (Saleem et al., 2015). While greater numbers of assigned easy items correlate positively with empathy, perspective taking, and trait prosocialty, higher numbers of assigned hard anagrams are associated with trait aggression. The tangram task has also successfully been used to measure aggressive behavior as a consequence of an experimental provocation (Saleem et al., 2015, studies 5 and 6). In comparison to other established measures of aggressive behavior like the hot sauce paradigm (Lieberman, Solomon, Greenberg, & McGregor, 1999) or the competitive reaction time task (Giancola & Zeichner, 1995), the tangram task is especially easy to adapt for online environments because it is exclusively text based and can be included into web surveys that run on all kinds of computers. In the current studies, feelings of anger as measured with the STAXI following the experimental Ó 2015 Hogrefe Publishing

J. Lutz: Crowdsourcing Data in Studying Anger and Aggression

manipulation were positively related to the assignment of very hard (r = .19, p < .001) and hard (r = .09, p < .01) anagrams and negatively to the assignment of easy (r = .20, p < .001) and medium (r = .21, p < .001) anagrams. This provides some support to the notion that the anagram task does indeed measure aggressive behavior driven by affective processes as predicted by the General Aggression Model (DeWall & Anderson, 2011).

The anagram assignment also included a check of participantsâ&#x20AC;&#x2122; compliance with the instructions. Even though they were asked to choose exactly seven anagrams for the other person to solve, it was technically possible to choose as many as they wanted to. Hence, choosing more or less than seven anagrams was used as an index of noncompliance. This check was included to test the possibility that the experience of frustration due to the experimental task may lead to reduced motivation to follow instructions or even to opposing behavior aimed at retaliating upon the experimenter.

Results Comparison of Samples Only participants who dropped out during the survey were excluded from the analyses of the online samples. In order to put the quality of the obtained data to the most conservative test, no cases were omitted because of timing plausibility (being too fast or too slow) or ambiguous survey behavior (e.g., not following instructions, see below).

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participants that dropped out without using the quit button came from the control condition (v2[1] = 12.30, p < .001), indicating that the few participants that actually dropped out during the frustrating anagram task predominantly used the controlled dropout option and received the debriefing.

Observed dropout was not related to experimental condition (v2s[1] 1.95, ps .36) in all other samples.

Gender and Age Composition In the laboratory sample, the proportion of men and women did not deviate significantly from a 50:50 distribution (Z = 0.89, p = .37). In all three AMT samples as well as in the Clickworker sample, more women than men participated but this trend was significant in neither of them (Zs 1.57, ps .12). A marginally significant difference was found for the Microworkers sample (Z = 1.90, p = .057) in favor of more male participants.

A one-way ANOVA with sample as independent and participant age as dependent variable revealed significant age differences (F[5, 711] = 35.82, p < .001, g2p = .20). Paired comparisons were conducted using Tukey-HSD post hoc tests. On average, participants in all online samples were in their 30s and thus significantly older than those in the laboratory sample (ps < .001). No significant age differences were found between AMT samples (ps .89). Participants in the Microworkers sample were significantly younger than those in the AMT Restricted and Clickworker samples (ps .03) but not significantly different from the AMT Non-restricted (p = .33) and Masters (p = .09) samples. AMT samples and the Clickworker sample did not differ significantly (ps .15).

Dropout Completion Time In all online samples, a number of participants started the experiment but then quit at some point. Dropout rates differed significantly between the five samples (v2[4] = 20.71, p < .001). The highest levels were found in the AMT Non-restricted (28% of those who initially opted in for the study), Microworkers (21%), and Clickworker (18%) samples. In the AMT Masters and AMT Restricted samples, the dropout rates were smaller (13% and 9%, respectively). The majority of participants that decided to drop out did so in an early stage of the survey.

In the AMT Masters sample, all dropouts were registered before the anagram task. In the Microworkers sample 95% of the dropouts quit before the experimental manipulation, in the AMT Non-restricted sample the rate was 88%, and in the Clickworker sample it was 78%. Only in the AMT Restricted sample 6 out of 12 participants dropped out during the anagram task. The Clickworker survey provided participants with the option to use a button to delete their data and immediately proceed to a full debriefing.

Almost half (45%) of the participants who decided to abort the experiment made use of this option and were redirected to the debriefing. The vast majority (16 out of 17) of the

Ă&#x201C; 2015 Hogrefe Publishing

A one-way ANOVA with sample as independent and completion time as dependent variable showed a significant effect (F[5, 719] = 36.17, p < .001, g2p = .20). Again, paired comparisons were conducted using Tukey-HSD post hoc tests. Compared to the average completion time in the laboratory session (M = 06:15, SD = 01:36), participants in the AMT Non-restricted (M = 08:37, SD = 02:32, p = .001), Microworkers (M = 10:05, SD = 06:46, p < .001), and Clickworker (M = 13:09, SD = 07:04, p < .001) samples took significantly more time to go through the experimental procedure. A marginal difference was found between the lab and the AMT Restricted samples (M = 07:56, SD = 02:33, p = .06). No significant timing difference was found between the laboratory and the AMT Masters sample (M = 07:03, SD = 02:02, p = .89).

Participants in the Microworkers sample took significantly longer than those of the AMT Masters and Restricted samples (ps .003). Participants in the Clickworker sample took significantly longer than participants in all other samples (ps < .001). This is obviously due to the incorporation of the positive affect induction task at the end of the survey

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which was only presented in the Clickworker sample. No significant differences were found between the AMT samples (ps .29). Means and standard deviations of completion times were somewhat biased by a small number of outliers in the Microworkers and Clickworker samples.

Removing participants with completion times of two standard deviations above the mean reduced the average time about 69 s in the Clickworker sample and 58 s in the Microworkers sample. Since the AMT platform imposes a set time limit on participants, AMT samples were not affected by outliers in the same way. Removing cases with completion times of two standard deviations above the mean resulted in average time reductions between 12 (AMT Masters) and 21 (AMT Restricted) seconds. Even though removing outliers reduced average completion times in all samples, the general pattern of sample differences was not affected. Further, completion time was not significant when included in a multivariate test of the experimental manipulation performed on the aggregated data of all samples (F[6, 707] = 0.75, p = .61, g2p = .01). Removing timing outliers in the univariate analyses led to virtually the same effect sizes compared to analyses comprising all cases (Dg2p = .00–.03).

Compliance Even though most participants (69%) in the laboratory experiment followed instructions and assigned exactly seven anagrams to another participant, 29% chose fewer anagrams and only two participants assigned more. Compliance in the frustration condition was not significantly different from the control group (v2[1] = 2.52, p = .13).

As in the laboratory, the majority of participants in the five online samples followed instructions and assigned exactly seven anagrams to the other person. Compared to the laboratory sample (69% compliance), only the Microworkers sample showed significantly lower compliance (57%, Z = 2.07, p < .05). The AMT Restricted (78%), Non-restricted (67%), and Clickworker (66%) samples did not differ significantly from the laboratory sample (Zs 1.68, ps .09). However, participants in the AMT Masters sample followed instructions even more conscientiously (88%) than in the laboratory sample (Z = 2.75, p < .01). Compliance was not affected by condition in the laboratory, all AMT samples, and the Microworkers sample (v2s[1] 2.63, ps .14), indicating that most frustrated individuals were as willing to faithfully continue with the experiment as their control-group counterparts. Only in the Clickworker sample lower compliance rates were found in the provocation condition (v2s[1] = 7.14, p < .01). Frustrated individuals in this sample assigned less anagrams (M = 5.92, SD = 1.68) than participants in the control group (M = 6.54, SD = 1.23, F[1, 144] = 6.50, p < .05, g2p = .04).

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Hypothesis Testing Laboratory Sample An initial multivariate analysis of variance (MANOVA) with frustration (vs. control) as independent variable and anger feelings, positive affect, arousal, aggressive, and prosocial behavior as dependent variables was computed to test the global effect of the experimental manipulation. Participant gender and age were entered as covariates. As hypothesized, there was a significant multivariate effect of the frustration manipulation (F[6, 116] = 13.14, p < .001, g2p = .41). Neither participants’ age (F[6, 116] = 0.47, p = .83, g2p = .02) nor gender (F[6, 116] = 1.31, p = .26, g2p = .06) exhibited a significant effect.

Means and standard deviations for all dependent variables as well as univariate test statistics are reported in Table 3.2 As expected, frustrated participants reported higher levels on both anger measures as well as increased arousal in comparison to participants in the control group.

In addition, the frustration manipulation led to lower positive affect. Participants in the laboratory sample chose anagrams mostly from the easy category (Measy = 2.28), followed by the medium category (Mmedium = 1.85), followed by the hard category (Mhard = 1.17). The fewest anagrams were chosen from the very hard category (Mvery hard = 1.17). Frustrated individuals acted significantly more aggressive by assigning more very difficult anagrams to another participant and less prosocial by assigning fewer easy anagrams.

Online Samples A MANOVA with condition (frustration vs. control) and sample as independent variables and anger, positive affect, arousal, aggressive, and prosocial behavior as dependent variables was employed to test the global effect of the experimental manipulation and differences between all samples. Participant gender and age were entered as covariates. The hypothesized multivariate main effect of the frustration manipulation was found to be significant (F[6, 698] = 36.06, p < .001, g2p = .24), as were a main effect of sample (F[30, 3,510] = 2.96, p < .001, g2p = .03) and a condition by sample interaction (F[30, 3,510] = 1.88, p < .05, g2p = .02). Significant multivariate effects were also found for participant gender (F[6, 698] = 3.71, p < .01, g2p = .03) and age (F[6, 689] = 3.19, p < .01, g2p = .03). Correlational analyses indicated that men tended to experience more anger postmanipulation (r = .13, p < .001; STAXI: r = .12, p < .001), and acted more aggressively (r = .09, p < .05) than women. Age was negatively related to post-manipulation anger (r = .09, p < .01; STAXI: r = .08, p < .05) and arousal (r = .08, p < .05).

Baseline measures were used as covariates for the univariate tests of post-manipulation variables. Because the STAXI was only assessed post-manipulation, the anger baseline was also used as covariate to test the effects on the STAXI scale. The effect on aggressive behavior was tested without a baseline covariate.

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Table 3. Descriptive statistics I – Laboratory, Microworkers & Clickworker samples Laboratory Frustration

Anger T1 Anger T2 STAXI Arousal T1 Arousal T2 Positive affect T1 Positive affect T2 Aggression Prosocial behavior

Control

M

SD

M

1.85 3.54 3.13 3.35 4.52 5.98 4.08 1.13 1.92

1.14 1.76 1.53 1.38 1.85 1.37 1.66 0.80 1.36

1.81 1.79 1.61 3.05 3.15 6.17 6.01 0.63 2.65

SD 1.24 1.35 1.01 1.36 1.39 1.61 1.67 0.67 1.45 Microworkers

Frustration

Anger T1 Anger T2 STAXI Arousal T1 Arousal T2 Positive affect T1 Positive affect T2 Aggression Prosocial behavior

g2p

0.051 50.91*** 55.39*** 2.311 20.91*** 1.061 61.21*** 13.21***1 8.95**1

.00 .29 .32 .02 .15 .01 .34 .09 .07

F(1,136)

g2p

0.162 6.86* 1.73 7.12**2 3.52 1.272 13.22*** 6.51*2 14.00***2

.00 .05 .01 .05 .03 .01 .09 .05 .09

Control

M

SD

M

2.73 3.40 2.82 4.55 4.97 5.94 4.61 1.23 1.55

2.06 2.17 2.12 1.99 1.95 1.70 1.82 0.85 1.12

2.61 2.66 2.36 3.65 3.91 5.63 5.31 0.85 2.36

Frustration

Anger T1 Anger T2 STAXI Arousal T1 Arousal T2 Positive affect T1 Positive affect T2 Aggression Prosocial behavior

F(1,120)

SD 1.86 2.03 2.14 1.96 2.07 1.79 1.96 0.96 1.44 Clickworker Control

M

SD

M

SD

F(1,134)

g2p

2.05 3.42 3.15 3.64 4.54 5.64 4.00 1.50 1.44

1.61 2.22 2.14 2.02 1.96 1.86 2.06 0.89 0.92

1.98 1.78 1.74 3.43 3.34 5.67 5.71 0.63 3.12

1.39 1.21 1.39 1.74 1.66 1.81 1.86 0.71 1.50

0.003 37.63*** 30.14*** 0.483 22.02*** 0.003 44.77*** 43.49***3 63.51***3

.00 .22 .18 .00 14 .00 .25 .24 .32

Notes. 1dfs = 1, 121; 2dfs = 1, 137; 3dfs = 1, 135; T1 = Pre-manipulation; T2 = Post-manipulation; All scale ranges: 1–9 except Aggressive behavior (0–5); Controlling for participant age, gender, and respective baseline scores. *p < .05; **p < .01; ***p < .001;

p < .10.

The multivariate main effect of sample was due to significant mean differences regarding positive affect (F[5, 703] = 2.26, p < .05, g2p = .02), arousal (F[5, 703] = 3.63, p < .01, g2p = .03), prosocial behavior (F[5, 703] = 3.49, p < .01, g2p = .02), and aggressive behavior (F[5, 703] = 3.55, p < .01, g2p = .03). Bonferroni-corrected paired comparisons revealed that positive affect in the AMT Masters sample was lower than in the laboratory and the AMT Non-restricted sample (ps < .05). Participants in the AMT Restricted and Microworkers samples reported significantly higher levels of arousal than those in the laboratory sample (ps < .05). Levels of aggressive behavior were significantly higher in the AMT Restricted and Nonrestricted samples than in the laboratory and AMT Masters Ó 2015 Hogrefe Publishing

Table

4.

Multivariate tests manipulation

Sample Laboratory Online samples AMT Masters AMT Restricted AMT Non-restricted Microworkers Clickworker Aggregated Online Aggregated AMT

of

the

experimental

F

df

p

g2p

13.14

6, 116

< .001

.41

2.78 5.27 10.49 5.49 17.43 30.48 14.95

6, 49 6, 116 6, 120 6, 132 6, 130 6, 583 6, 303

< < < < < <

.02 .001 .001 .001 .001 .001 .001

.25 .21 .34 .20 .45 .24 .23

Note. Controlling for participant age and gender.

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Table 5. Descriptive Statistics II – AMT samples AMT Masters Frustration

Anger T1 Anger T2 STAXI Arousal T1 Arousal T2 Positive affect T1 Positive affect T2 Aggression Prosocial behavior

Control

M

SD

M

1.43 3.11 2.57 3.29 4.89 5.29 3.45 1.00 2.43

0.75 2.32 1.99 1.41 1.97 1.49 1.74 0.86 1.50

1.74 1.78 1.32 3.17 3.50 5.14 4.84 0.50 3.20

Frustration

Anger T1 Anger T2 STAXI Arousal T1 Arousal T2 Positive affect T1 Positive affect T2 Aggression Prosocial behavior

1.17 1.17 0.58 1.70 2.03 2.01 2.23 0.68 1.21 AMT Restricted

F(1,53)

g2p

1.221 13.28** 13.35** 0.191 6.72* 0.061 17.16*** 5.66*1 4.83*1

.02 .20 .20 .00 .11 .00 .25 .09 .08

F(1,120)

g2p

0.352 25.67*** 10.85** 0.722 16.19*** 0.542 24.69*** 2.102 1.762

.00 .18 .08 .01 .12 .00 .17 .02 .01

Control

M

SD

1.99 3.76 2.70 3.62 5.20 5.97 4.11 1.38 2.10

1.41 2.50 1.98 2.10 1.88 1.59 2.18 1.37 1.60

M

SD

2.13 1.39 2.24 1.53 1.91 1.42 3.32 1.75 3.83 2.05 5.75 1.66 5.42 1.85 1.03 1.27 2.46 1.46 AMT Non-restricted

Frustration

Anger T1 Anger T2 STAXI Arousal T1 Arousal T2 Positive affect T1 Positive affect T2 Aggression Prosocial behavior

SD

Control

M

SD

M

SD

F(1,124)

g2p

2.43 3.93 3.50 4.04 4.43 6.16 4.27 1.47 1.85

1.91 2.37 2.31 2.35 2.08 2.04 2.27 1.25 1.45

1.91 1.62 1.70 3.77 4.05 5.88 5.87 0.97 2.54

1.48 1.18 1.19 2.41 2.44 2.24 2.31 0.95 1.37

3.09 3 46.04*** 28.39*** 0.503 0.50 0.563 31.05*** 7.15*3 8.22**

.02 .27 .19 .00 .00 .00 .20 .05 .06

Notes. 1dfs = 1, 54; 2dfs = 1, 121; 3dfs = 1, 125; T1 = Pre-manipulation; T2 = Post-manipulation; All scale ranges: 1–9 except Aggressive behavior (0–5); Controlling for participant age, gender, and respective baseline scores. *p < .05; **p < .01; ***p < .001; p < .10.

sample (ps < .06). No significant differences between the laboratory and the online samples were found regarding prosocial behavior but participants in the AMT Masters sample acted significantly more prosocial than those in the Microworkers (p < .01) and the AMT Non-restricted samples (p = .059). Participants in the online samples chose anagrams mostly from the easy category (Measy = 2.22), followed by the medium category (Mmedium = 1.85), followed by the hard category (Mhard = 1.17). The fewest anagrams were chosen from the very hard category (Mvery hard = 1.09).

This distribution is very similar to the laboratory data.

3

The multivariate main effect of the frustration manipulation was found to be significant in all online samples (see Table 4). Like participants in the laboratory, the experience of frustration led individuals in the online samples to report less positive affect, elevated levels of anger and arousal and made them act more aggressively and less prosocial toward an uninvolved person. Means and standard deviations as well as univariate test statistics3 and effect sizes for all dependent variables and samples are reported in Tables 3 and 5. A graphical comparison of aggressive behavior in the experimental groups for all samples is presented in Figure 1.

Controlling for age, gender, and respective baseline measures. Previous research has provided some evidence supporting the robustness of F-tests even with skewed data which is typical for experiments on anger and aggressive behavior (Harwell, Rubinstein, Hayes, & Olds, 1992; Schmider, Ziegler, Danay, Beyer, & Bühner, 2010).

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J. Lutz: Crowdsourcing Data in Studying Anger and Aggression

Figure 1. Mean numbers of assigned very hard anagrams (aggressive behavior). Error bars represent standard errors.

As indicated by the significant multivariate interaction, the size of the experimental effects varied across samples (see Table 4). Effect sizes in the AMT and Microworkers samples (g2p = .20–.34) were smaller than in the laboratory (g2p = .41). However, the effect size obtained from the Clickworker data (g2p = .45) is of almost equal size as in the laboratory. The difference between the effect in the aggregated online samples (g2p = .24) and the laboratory was Dg2p = .17. Effect sizes also varied between the online samples. For the AMT samples, the biggest multivariate effect was found in the Non-restricted sample (g2p = .34), followed by the Masters (g2p = .25) and Restricted (g2p = .21) samples. The effect found in the Microworkers sample (g2p = .20) is almost the same as in the AMT Restricted sample. The difference between the aggregated combined effect in the three AMT samples (g2p = .23) and the laboratory was Dg2p = .18.

The results of the univariate tests (Tables 3 and 5) shed further light on the nature of the observed effect size differences between online samples and the laboratory sample as well as within the online samples. As in the laboratory, all hypothesized effects emerged significant in the Clickworker and AMT Masters samples. Compared to the laboratory, effect sizes on the affective measures were somewhat smaller in the Clickworker as well as in the AMT Masters sample (Dg2p = .07–.14). Effect sizes for the behavioral and arousal measures in the AMT Masters sample were almost identical to the effects found in the laboratory. However, behavioral effects in the Clickworker sample were substantially stronger than in the laboratory (Dg2p = .15/.25). In the AMT Non-restricted sample, five out of six effects were found to be statistically reliable. The experimental manipulation failed to induce arousal in this sample. While the effect sizes on the behavioral measures and the three-item anger measure were similar to the laboratory, the effects for positive affect and the STAXI were smaller than in the laboratory (Dg2p = .14/.13). In each of the AMT Restricted and Microworkers samples, four out of six hypothesized effects emerged significant. Effect sizes on the affective measures Ó 2015 Hogrefe Publishing

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in the AMT Restricted sample were lower than in the laboratory and similar to the other online samples except for the STAXI, which was substantially lower (g2p = .08). However, no behavioral effects were found to be significant in the AMT Restricted sample. The Microworkers sample showed clearly the smallest effects on the affective measures, while results for the measures of aggressive and prosocial behavior were similar to those of the laboratory sample. No significant effects were found for the STAXI and the arousal measure in this sample.

Since participants in all online samples were significantly older than those in the laboratory sample and higher age was found to be associated with less anger affect and arousal after the experimental manipulation, further analyses were conducted to test if age differences could explain the smaller effect sizes in the online samples. If the smaller effects in four of the five online samples were due to a higher proportion of older participants compared to those in the laboratory sample, a separate analysis of only the younger online participants should yield higher effect size estimates. The cutoff age was set to under 30 years which corresponds to the average age of the laboratory sample plus 2 standard deviations. Since the exclusion of all participants aged 30 or older reduced online sample sizes by more than 50%, the age-restricted analyses were conducted on the pooled data of all online samples and the aggregated AMT samples, respectively. The age-restricted multivariate effect in the aggregated online samples was significant and marginally higher than with older participants included (F[6, 217] = 13.44, p < .001, g2p = .27). The age-restricted multivariate effect in the aggregated AMT samples was significant and higher than with older participants included (F[6, 112] = 7.44, p < .001, g2p = .29). Even though these results point to stronger effects in younger participants, the differences compared to the complete datasets are only small (Dg2p = .03–.06). Further, the effect sizes obtained from the age-restricted analyses are still smaller than those from the laboratory and Clickworker samples.

The Clickworker survey included an additional positive affect induction task and subsequent final measurement of anger, positive affect, and arousal at the end of the experiment. The multivariate effect of the frustration task was no longer significant after the positive affect induction task (F[3, 133] = 0.62, p = .61, g2p = .01), indicating that the affective consequences of the frustrating task were either successfully buffered by the positive affect induction or had worn out by that time, as they did in the pilot study.

Discussion The present study was conducted to explore if online crowdsourcing markets could be used to obtain reliable data in studies that incorporate the experimental induction of aversive affective states. In five online studies, using three crowdsourcing platforms as participant pools, the results of a laboratory experiment on aggressive behavior could be replicated. The overall effect of the experimental manipulation found to be significant in a laboratory sample with Social Psychology 2016; Vol. 47(1):38–51

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German students also emerged in all online samples. However, effect sizes were smaller in crowdsourcing samples with non-German participants while a crowdsourcing sample with exclusively German participants yielded virtually the same effect size as in the laboratory. Further, age differences between crowdsourcing and laboratory samples had an influence on effect sizes.

In accordance with previous research (Buhrmester et al., 2011; Mason & Suri, 2012), most participants in the crowdsourcing samples were older than subjects in the college sample. The proportion of men and women varied between samples but there was only a marginally significant difference between the number of men and women in the Microworkers sample. Together with most crowdsourcing markets’ built-in options to address only participants from specified countries or other screening criteria, this indicates that crowdsourcing samples are potentially more diverse than college samples and might help researchers in generalizing their findings.

As in most online researches (Mason & Suri, 2012; Reips, 2002), a certain degree of participant dropout was observed in all crowdsourcing samples. But importantly, this dropout was not affected by condition in five out of six samples. Even though participants experienced negative affect after engaging in a frustrating task, they did not abort the experiment as a consequence. Also, most participants that prematurely quit the experiment did so in a very early stage of the survey before the experimental manipulation. In the Clickworker sample, a ‘‘controlled dropout’’ option was introduced to make sure that even participants who decided to quit the experiment received a full debriefing. The results suggest that participants made indeed use of this option, especially those dropping out from the frustration group.

Hence, providing an explicit exit protocol may prove an efficient strategy to deal with problems arising from dropout in studies that involve the induction of aversive affective states.

In terms of psychometric indices and general survey behavior, online and laboratory data proved to be quite similar. Reliability coefficients for all measures in the online samples indicated sufficient consistencies and were in part even higher than those obtained from the laboratory data.

Similarly, compliance in the online samples was by and large comparable to those of subjects in the laboratory sample. While the Microworkers sample showed lower rates of compliance, the AMT and Clickworker samples did not differ from the laboratory data or even outperformed them in the case of the Masters sample. As with dropout rates, participants’ compliance was not affected by experimental condition in five out of six samples, indicating their commitment to the faithful continuation of the study, despite the frustrating experience. Only in the Clickworker sample a significant difference between the experimental groups was found. On average, frustrated participants in this sample assigned less anagrams than those in the control group.

All but the most qualified AMTworkers took significantly longer than participants in the laboratory to go through the experimental procedure. The average completion times of all AMT samples were still within a plausible range. Only the Microworkers sample took noticeably longer on average.

Completion times in the Clickworker sample were elevated Social Psychology 2016; Vol. 47(1):38–51

due to the extended experimental procedure and are thus not comparable to the other samples’ timings. Longer completion times in the crowdsourcing samples might point to issues with non-attentiveness or distraction in some of the online samples (Chandler et al., 2014; Goodman et al., 2013). On the other hand, timing differences might also be due to greater task familiarity of student participants in our laboratory sample.

Psychology students participate in a lot of studies during their undergraduate education and should therefore be highly trained and comparatively fast in filling out questionnaires. Analogously, AMT is increasingly used by academic requesters and especially frequent workers might have some experience with scientific surveys. By contrast, Microworkers is less frequently used by academic requesters (Hirth et al., 2011), and workers on this platform are probably less familiar with survey-like tasks.

The comparisons of multivariate effect sizes between the online and the laboratory samples as well as the results of the age-restricted analyses in the online samples point to a significant role of sample composition. In comparison to the German laboratory data, lower effect sizes were obtained from all AMT samples as well as from the Microworkers sample. This was especially due to smaller effects on the affective measures. A small part of these differences seems to be attributable to age differences between the laboratory and the crowdsourcing samples. Participants in the online samples were older on average and age was negatively related to post-manipulation anger and arousal. This corresponds to results from previous research indicating that feelings of anger (Phillips, Henry, Hosie, & Milne, 2006) and aggressive behavior (Krahé & Fenske, 2002) decline with age. Accordingly, running analyses only on younger online participants yielded somewhat stronger effects.

But even these age-restricted effect sizes were smaller than in the laboratory. In comparison, the multivariate effect size obtained from the German crowdsourcing sample was of almost the same size as in the laboratory, even a bit higher.

Univariate tests revealed that while effects on the affective measures were somewhat smaller in the Clickworker sample, effects regarding aggressive and prosocial behavior were substantially stronger than in the laboratory.

These results strongly suggest that effect size estimates from crowdsourcing samples are essentially comparable to those from laboratory data. However, researchers should be aware of the potential influence of sample composition on effect sizes and carefully select the crowdsourcing platform to sample from as well as potential prescreening criteria like gender, age, or nationality, depending on the respective research question.

Even though preselecting highly qualified participants in the AMT samples led to less dropout, better compliance, and timings most similar to the laboratory data, results regarding the effects of preselection on the size of the manipulation effect were less clear. The multivariate effect in the AMT sample without any restrictions on prior qualification was somewhat bigger than in the AMT Masters sample. However, all univariate tests of the manipulation effect in the AMT Masters sample emerged significant with effect sizes most comparable to the laboratory while in the AMT Non-restricted sample the effect on arousal could not Ó 2015 Hogrefe Publishing

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be replicated. Manually preselecting qualified participants as suggested in the literature (Peer et al., 2014) did not produce data of better quality. Quite the contrary, no significant effects were found on the behavioral measures in the AMT Restricted sample. Since anger is assumed to be the driving affective force for both measures, these results may be explained by the comparably smaller effect of the frustration manipulation on the STAXI anger measure in this sample.

The Microworkers and Clickworker samples, which were both not restricted regarding prior qualification, differed most significantly from each other. While generally the smallest effect sizes were obtained in the Microworkers sample, effects on the behavioral measures in the Clickworker sample were even stronger than in the laboratory data. Since participants in the Microworkers sample also showed significantly lower compliance, the reduced effect sizes could at least be partially due to reduced attentiveness in this sample.

Albeit some evidence in the present data speaks in support of the notion that preselecting high-qualification workers improves data quality (Peer et al., 2014), participants that are not prescreened may be motivated and conscientious enough to produce data that is sufficiently similar to laboratory data in affectively involving experiments.

Clearly, more research is needed on this matter. While no clear conclusion can be drawn regarding the impact of prescreening based on prior qualification, it seems fair to say that on average the AMT samples provided effect size estimates that were somewhat closer to those obtained from the laboratory data compared to the Microworkers sample.

Interestingly, this was found to be the case even though participants in the Microworkers sample received a significantly higher reimbursement than those in the AMT samples. But even disregarding the Microworkers sample, the overall experimental effect for all AMT samples was smaller than in the laboratory and Clickworker samples.

One limitation of the present study is its inability to identify the ultimate cause of the reported differences in effect sizes between the German and the non-German online samples. Because it is known that anger and aggression are construed differently in various cultures (Severance et al., 2013), the identified effect size differences may be attributable to cultural differences between German and US/Indian participants. However, it remains unclear why exactly German participants would react stronger to the experimental manipulation than people from the US or India. Apart from culture/nationality, there might be possible alternative explanations. It has been shown, that non-naivety leads to lower effect sizes in online samples (Chandler et al., 2015). Since the Clickworker platform has only recently been made accessible for survey-based research, one could assume that participants sampled from this platform are not yet used to psychological research and hence truly naïve. In comparison, AMT is frequently used for all kinds of psychological studies and regular AMT workers may become very familiar with certain paradigms (Chandler et al., 2014). On the other side, measures were taken in the AMT samples to ensure participants’ naivety, and the anagram frustration paradigm was probably new to the vast majority of the participants. Further, the Microworkers platform is less used for psychological Ó 2015 Hogrefe Publishing

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research than AMT and still the effect sizes obtained from that sample were smaller than those from all other samples.

Also, little is known about the Clickworker population.

In the presented data, Clickworker participants were somewhat older than participants from other crowdsourcing markets but no information is available on extended demographics or even the distribution of psychological variables in this population. In comparison, there is evidence that AMT samples differ from college and community samples on measures of extraversion, openness to experience, selfesteem, and emotional stability (Goodman et al., 2013), as well as social anxiety (Shapiro, Chandler, & Mueller, 2013). No research exists on differences between crowdsourcing and college samples regarding trait anger, aggressiveness, or other related dimensions. Therefore, it cannot be ruled out that systematic differences in these domains may have had an influence on the reported effect sizes in addition to the actual method of data collection and nationality. Further research replicating the present findings and extending them to other affectively involving situations is needed to establish that effect size estimates from crowdsourcing samples in affectively involving research domains are indeed trustworthy and basically equivalent to laboratory data.

Of course, ethical considerations will preclude some social psychological paradigms from online administration.

In the current study, a lab-pretested manipulation was employed that induced a short-lived aversive affective state.

Ideally, researchers should only adapt experimental paradigms to online studies which have proven to be safe in a laboratory setting. To take care of online participants in the best possible way, measures like the ‘‘controlled dropout’’ option introduced in the Clickworker sample may be helpful to make sure all participants receive a full debriefing. Further, simple positive affect induction techniques can be used to reduce residual negative affect after the actual experiment. Finally, prescreening and excluding especially vulnerable individuals may be advisable if the experimental manipulation taps into sensitive areas. In studies on aggressive behavior, researchers may consider excluding highly aggressive or anger prone people from participating in online experiments which incorporate frustration or provocation manipulations. This could easily be done by assessing trait anger or aggression preceding the actual experiment using standard self-reports.

In conclusion, the present study provides further evidence that crowdsourcing markets can be used as reliable participant pools for affectively involving experimental studies in social psychology and related fields. The obtained data proved to be sufficiently similar to laboratory data, especially when participants of the same nationality were recruited. The results further show that even though Mechanical Turk is the crowdsourcing market most often used for psychological online research, data of excellent quality can also be collected through alternative marketplaces. This may be found especially interesting by some in the light of the recent increase in commission rates by Amazon. Prescreening participants based on prior performance might have some advantages but may not be a necessary to collect reliable data. More research is needed with regard to this question.

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Hence, acquiring samples from crowdsourcing platforms might prove helpful also for researchers in fields that usually rely on classic approaches to data collection. Especially the potential to replicate findings on a larger scale using sufficiently-powered and diverse samples and thereby increasing confidence in findings seems promising. However, researchers should be aware of the inherent differences between online and laboratory experimentation as well as issues regarding demographics and cultural variation when interpreting and comparing effect sizes obtained from crowdsourcing samples.

Acknowledgments The author gratefully acknowledges the help of Barbara Krahé who offered valuable comments on an earlier draft of this manuscript.

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Received March 20, 2015 Revision received July 16, 2015 Accepted July 16, 2015 Published online December 30, 2015 Johannes Lutz University of Potsdam Department of Psychology Karl-Liebknecht-Straße 24/25 14476 Potsdam Germany Tel. +49 331 977-2954 Fax +49 331 977-2795 E-mail jlutz@uni-potsdam.de

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Original Article

Heart Versus Mind How Affective and Cognitive Message Frames Change Attitudes Fabian A. Ryffel and Werner Wirth Institute of Mass Communication and Media Research, University of Zurich, Switzerland Abstract. Several researchers have pursued the question of whether affective or cognitive persuasion appeals are more successful in changing attitudes. The vast majority of studies in this field have found that the persuasiveness of affective and cognitive appeals depends on the extent to which recipients’ existing attitudes are based on affect or cognition: Affective messages are more successful in changing affect-based attitudes; cognitive messages are more successful in changing cognition-based attitudes. However, research to date has not uncovered the processes leading to these effects. In the present article it is argued that there are two plausible explanations. First, matching messages to informational attitude bases might heighten message scrutiny. This would mean that a central process underlies the effects. Second, a peripheral process might account for the effects. Specifically, processing fluency might act as a peripheral cue. The results of an experimental study clearly suggest that that processing fluency underlies the effects.

Keywords: matching, mismatching, persuasion, processing fluency, message scrutiny

Attitudes have been conceptualized as consisting of an affective and a cognitive component (e.g., Breckler, 1984; Breckler & Wiggins, 1989). The affective component consists of emotions and feelings toward an attitude object, the cognitive component refers to beliefs and judgments about an attitude object (Breckler & Wiggins, 1991). Depending on the importance of affective and cognitive information contributing to an overall evaluation, attitudes can be located within a continuum ranging from affect based to cognition based (Edwards, 1990). That is, attitudes can be either primarily based on affect or on cognition: ‘‘Conceptualizing attitudes as having affective (emotional) and cognitive (belief) bases has been one of the most popular means of classifying the different types of information upon which attitudes are based’’ (Petty, Wegener, & Fabrigar, 1997, p. 613). These differences in informational attitude bases have extensive implications for persuasion. Previous studies have described matching effects, that is, that emotional persuasion appeals are more successful in changing affect-based attitudes, while informational appeals are more successful in changing cognition-based attitudes (e.g., Fabrigar & Petty, 1999).

However, one previous study indicated a mismatching effect (Millar & Millar, 1990). In this study, affective persuasion appeals were more successful against cognition-based attitudes than against affect-based attitudes, while rational appeals were more successful in changing affect-based attitudes than cognition-based attitudes. Attempting to explain this contradiction in previous research, some researchers have suggested that recipient characteristics may moderate the occurrence of matching and mismatching effects.

Social Psychology 2016; Vol. 47(1):52–62 DOI: 10.1027/1864-9335/a000257

Specifically, Millar (1992) found that participants with prior experience with an attitude object were persuaded more effectively by mismatching than by matching appeals. This experiment by Millar (1992) also revealed a matching effect for participants with little prior experience with an attitude object. More recently, Clarkson, Tormala, and Rucker (2011) found mismatching effects for attitudes held with low attitude certainty, along with matching effects for attitudes held with high certainty (see also Ryffel, Wirz, Kühne, & Wirth, 2014). On the one hand, these valuable efforts indicate that recipient characteristics moderate the occurrence of matching and mismatching effects. However, since direct experience with an attitude object is positively related to attitude certainty (e.g., Fazio & Zanna, 1978), the results by Millar (1992) and Clarkson and colleagues (2011) are somewhat contradictory on the other hand. Thus, we still do not know under what circumstances matched or mismatched messages will be more effective in creating attitude change.

To clarify why mismatching informational attitude bases may sometimes be more successful, we need to learn more about the processes behind the effects. Therefore, drawing on dual process theories, we consider the question of whether matching effects between message frames and informational attitude bases are driven by central or peripheral processes. Specifically, matching persuasion messages to informational attitude bases potentially heightens message scrutiny, meaning that a central process might underlie the effects. Contrarily, heightened processing fluency of matching persuasion messages might act as a peripheral cue influencing perceived message verity, meaning that a peripheral process might underlie the effects.

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Matching Effects in Persuasion Scholars studying persuasion agree that persuasive messages are more successful in changing attitudes when their presentation and contextualization is tailored to recipients’ preexisting mindsets (e.g., DeBono & Rubin, 1995; Petty, Wheeler, & Bizer, 2000). A large body of literature has been published on matching effects between message frames and informational attitude bases (e.g., Edwards & von Hippel, 1995; Fabrigar & Petty, 1999). In these studies, affectively and cognitively based attitudes toward fictitious attitude objects have been induced and then challenged by either affective or cognitive appeals using various manipulations of affect and cognition, as well as different attitude objects. More recently, some authors have presented innovations in how one can study affective and cognitive matching effects: Instead of inducing affectively and cognitively based attitudes prior to challenging them, these authors focused on personality traits when investigating interactions between affective and cognitive message frames and recipient characteristics. For instance, See, Petty, and Fabrigar (2008) used structural attitude bases and attitude meta-bases when investigating affective and cognitive matching effects.

See and colleagues (2008) conceptualize structural attitude bases as a global tendency of individuals to base their attitudes on either affect or cognition, while meta-bases are conceptualized as subjective perceptions of one’s own affective versus cognitive attitude bases across a variety of objects. Results by See and colleagues (2008) suggest that affective and cognitive message frames matching these trait-like constructs produce more persuasion than mismatching frames.

Likewise, Haddock, Maio, Arnold, and Huskinson (2008) found that the personality traits need for affect (Maio & Esses, 2001) and need for cognition (Cacioppo & Petty, 1982) influenced recipients’ susceptibility to affective and cognitive persuasion messages: Participants high in need for affect (cognition) were more susceptible to affective (cognitive) messages.

Besides affective and cognitive matching effects, several other matching effects in persuasion have been reported in previous studies. For example, function matching effects have received considerable attention (e.g., DeBono & Rubin, 1995). Function matching effects are based on the assumption that people hold attitudes because they serve particular functions, such as expressing values or fitting in with others (Katz, 1960). Function matching means that persuasive appeals are more successful in changing attitudes when they address the particular function served by an attitude, rather than when they do not (e.g., Lavine & Snyder, 1996). Another form of matching effects that has been investigated in the context of persuasion is selfschema matching. This effect is based on the understanding that people hold beliefs about their own personality, such as about whether they are outgoing or shy, or whether they consider themselves to be analytical or intuitive decisionmakers (e.g., Wheeler, Petty, & Bizer, 2005). Studies have shown that matching messages to the recipient’s selfschemas enhances persuasion (e.g., Brock, Brannon, & Bridgwater, 1990). Research has also shown that a 2015 Hogrefe Publishing

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regulatory fit increases persuasion. Regulatory focus theory (Higgins, 1998) suggests that people have two distinct selfregulation strategies. The first strategy, promotion focus, emphasizes the pursuit of gains, while the other, prevention focus, emphasizes the avoidance of losses. When engaged in a promotion-focused self-regulatory process, the achievement of positive outcomes is salient and people strive to achieve goals; when prevention-focused, potential losses are salient and people are motivated to avoid losses (Brockner & Higgins, 2001). Several studies have shown that messages are more persuasive when they are framed to match recipients’ regulatory foci (e.g., Cesario, Grant, & Higgins, 2004; Lee & Aaker, 2004).

Explaining Matching Effects in Persuasion The aim of the present article is to identify the processes driving matching effects between affective and cognitive message frames and informational attitude bases. In seeking to explain different kinds of matching effects in persuasion, scholars often reference dual process theories (e.g., Petty et al., 1997, 2000). According to the elaboration likelihood model of persuasion (Petty & Cacioppo, 1986), variables such as the source of information or a match between message frame and informational attitude basis can affect persuasion in four ways: ‘‘(1) by serving as an argument, (2) by serving as a cue, (3) by determining the extent of elaboration, and (4) by producing a bias in elaboration’’ (Petty & Wegener, 1999, p. 51). Two of these ways have been considered plausible explanations for matching effects (Petty et al., 1997).

First, it has been argued that matching recipients’ mindsets is a successful persuasion strategy due to peripheral processes (e.g., Petty et al., 1997). This means that the match between the message and the structure underlying an attitude serves as a peripheral cue. That is, recipients might be persuaded by affective or cognitive appeals simply because they notice that the message resonates with their existing mindset. Moreover, it has been argued that matching appeals are more successful in changing attitudes because they can be processed more fluently (Lee & Aaker, 2004). Fluency has been shown to act as a cue that influences the perception of encountered stimuli. Specifically, individuals perceive information that is processed fluently as more probably true (Dechêne, Stahl, Hansen, & Wänke, 2009; Unkelbach, Bayer, Alves, Koch, & Stahl, 2011).

Therefore, appeals that can be processed fluently are more persuasive than appeals that cannot be processed fluently.

However, to assume that peripheral processes account for matching effects between message frames and informational attitude bases does not necessarily mean that recipients base their judgments solely on peripheral cues when they process matching information. Rather, a match between message frames and informational attitude bases is assumed to provide recipients with an additional peripheral cue. Hence, reaching a satisfactory level of confidence regarding a judgment is expected to require less cognitive effort. Lee and Aaker (2004) provide evidence for the processing fluency explanation in the case of the regulatory Social Psychology 2016; Vol. 47(1):52–62

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fit effect on persuasion. In their experiments, participants experienced greater processing fluency when the message matched their regulatory focus than when the message mismatched the regulatory focus. Thus, they concluded that processing fluency underlies the regulatory fit effect on persuasion. There is also evidence suggesting that fluency can serve as a cue in the case of matches between affective and cognitive message frames and informational attitude bases: Ryffel et al. (2014) found matching effects for affect- and cognition-based attitudes held with high certainty (i.e., instances when participants had a great deal of knowledge about the attitude object), as well as mismatching effects for low certainty attitudes (i.e., instances when participants had little prior knowledge; see also Clarkson et al., 2011). Since prior knowledge facilitates the experience of processing fluency (Schwarz & Clore, 2007), these results make sense in light of the fluency explanation: Participants with high attitude certainty were more likely to experience processing fluency, which may have led to the matching effects obtained in the high certainty conditions. Mayer and Tormala (2010) primed either affective or cognitive thoughts about a well-known object (blood donation) rather than inducing attitudes based on either affect or cognition.

The researchers then presented participants with first-person accounts that were either framed in terms of the source’s thoughts (‘‘I think. . .’’) or feelings (‘‘I feel. . .’’).

Mayer and Tormala (2010) found that messages that matched the previously primed thoughts were processed more fluently than mismatching messages. Likewise, See, Petty, and Fabrigar (2013) found that participants with affective structural attitude bases spent a smaller proportion of time reading affective than cognitive information. Even though the authors did not measure processing fluency, this result may also indicate that participants processed matching information more fluently than mismatching information. Therefore, processing fluency could also explain why affective and cognitive information matching the recipients’ informational attitude bases is more persuasive than mismatching information. If that is the case, mismatching appeals should be scrutinized more carefully than matching appeals (Petty et al., 1997). However, although this explanation is plausible, empirical evidence is lacking.

Second, matching effects have been explained through heightened message elaboration (Petty & Wegener, 1998).

That is, persuasive messages speaking directly to the structure underlying an attitude may be perceived as more relevant, which heightens processing motivation. For example, in the case of function matching effects, Petty and Wegener (1998) found an interaction between argument strength and functional match. Specifically, the authors found that when weak arguments are presented, matching an attitude’s function leads to less persuasion than mismatching the attitude’s function. Petty and Wegener (1998) explain their findings by stating that functionally matching arguments heighten message elaboration. As a result, weak arguments are more likely to be recognized as such when they match the functional basis underlying the attitude, which inhibits persuasion. Similarly, Wheeler and colleagues (2005) found argument strength effects for self-schema matching. In their study, argument-quality effects were more than four times Social Psychology 2016; Vol. 47(1):52–62

larger when the presented messages matched participants’ self-schemas. These results suggest that matching arguments heighten message elaboration. Moreover, results from previous research suggest that the heightened processing motivation explanation might also apply to affective and cognitive matching effects. Specifically, Haddock and colleagues (2008) found that individual differences in need for affect (need for cognition) predicted the amount of information correctly recognized from an affective (cognitive) message. These results indicate that ‘‘matched information was processed with greater depth than nonmatched information’’ (Haddock et al., 2008, p. 7).

Likewise, See and colleagues (2008, 2013) found that affective (cognitive) attitude meta-bases predicted longer reading times for affective (cognitive) information. These results also suggest that participants scrutinize information matching their attitude meta-basis more carefully than mismatching information. If heightened message scrutiny explains why message frames matching recipients’ informational attitude bases are more persuasive than mismatching frames, matching appeals should be scrutinized more carefully than mismatching appeals. In this case, persuasion would result from elaborating on substantive arguments rather than from relying on cues. Although this rationale is logical, it has never been empirically validated.

Hypotheses The previous section discussed that matching effects could be due to heightened message scrutiny or heightened processing fluency. The following experiment manipulates the strength of the persuasion appeals to differentiate these possibilities. Since greater appeal strength effects suggest greater appeal scrutiny (Petty & Wegener, 1999, p. 53), the strength of the persuasion appeals is manipulated in an experiment.

We start with the assumption that matching effects between affective and cognitive message frames and informational attitude bases are the result of a peripheral process (Petty et al., 1997). This reasoning suggests that appeals matching the recipients’ informational attitude bases are successful in changing attitudes simply because they appeal to recipients’ existing mindsets, and can be processed fluently. That is, heightened processing fluency might serve as a peripheral cue indicating that the persuasion message is true. If peripheral processes account for the effects, one would expect matching effects for weak appeals, as weak arguments are less likely to be recognized as such in the assumed process. In contrast, weak mismatching messages cannot be processed as fluently as weak matching messages. Thus, weak mismatching messages are more likely to be recognized as unconvincing and should therefore not entail persuasion. Accordingly, the following hypotheses are advanced.

Matching hypotheses for weak appeals: Hypothesis 1a (H1a): Weak cognitive appeals are more successful in changing cognition- than affectbased attitudes.

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Table 1. Hypotheses of the present study. Hypotheses 1a–1d theorize that peripheral processes account for matching effects between message frames and informational attitude bases. Hypotheses 2a–2d instead theorize that heightened message scrutiny underlies these effects.

Hypothesis

Strength of the persuasion appeal

1a 1b 1c 1d

2a 2b 2c 2d

Weak Strong

Weak Strong

Framing of the persuasion appeal

If peripheral processes account for matching effects Cognitive Cognitive Affective Affective Cognitive Affective Affective Cognitive If heightened message scrutiny accounts for matching effects Cognitive Affective Affective Cognitive Cognitive Cognitive Affective Affective

Hypothesis 1b (H1b): Weak affective appeals are more successful in changing affect- than cognitionbased attitudes.

If this process underlies the effects, one would also expect mismatching effects for strong persuasion messages.

This is because strong matching appeals are less likely to be recognized as strong when they are processed less thoroughly. In contrast, strong mismatching appeals are more likely to be recognized as strong because mismatching messages are scrutinized more thoroughly than matching messages. Therefore, strong mismatching messages should be more persuasive than strong matching messages.

Mismatching hypotheses for strong appeals: Hypothesis 1c (H1c): Strong cognitive appeals are more successful in changing affect- than cognitionbased attitudes.

Hypothesis 1d (H1d): Strong affective appeals are more successful in changing cognition- than affectbased attitudes.

If, however, appeals matching the recipients’ informational attitude bases heighten message scrutiny, one would expect the same pattern of results that has been found in studies investigating the processes behind function (Petty & Wegener, 1998) and self-schema matching (Wheeler et al., 2005). Specifically, one would expect mismatching effects for weak persuasive messages. This is because weak matching appeals are more likely to be recognized as unconvincing if matching heightens message scrutiny.

Mismatching hypotheses for weak appeals: Hypothesis 2a (H2a): Weak cognitive appeals are more successful in changing affect- than cognitionbased attitudes.

Hypothesis 2b (H2b): Weak affective appeals are more successful in changing cognition- than affectbased attitudes.

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Type of attitude that is expected to be more susceptible to the appeal

Type of effect Matching Mismatching

Mismatching Matching

If heightened message scrutiny accounts for matching effects between message frames and informational attitude bases, one would also expect matching effects for strong persuasive messages. This is because strong appeals should exert greater influence on attitudes when message scrutiny is heightened by matching an appeal to recipients’ informational attitude bases.

Matching hypotheses for strong appeals: Hypothesis 2c (H2c): Strong cognitive appeals are more successful in changing cognition- than affectbased attitudes.

Hypothesis 2d (H2d): Strong affective appeals are more successful in changing affect- than cognitionbased attitudes.

These hypotheses are contradictory. Specifically, if Hypotheses 1a–1d are confirmed, Hypotheses 2a–2d must be rejected. This pattern of results would suggest that peripheral processes account for matching effects between message frames and informational attitude bases. In contrast, if Hypotheses 2a–2d are confirmed, Hypotheses 1a– 1d must be rejected. This pattern of results would indicate that heightened message scrutiny instead leads to the effects. The hypotheses are summarized in Table 1.

Method An experiment tested the hypotheses by adapting previous studies’ procedures (e.g., Edwards & von Hippel, 1995; Fabrigar & Petty, 1999). The experiment consisted of four phases. In the first phase, participants were presented with an induction article providing information about a fictitious attitude object. That article was designed to induce attitudes primarily based on either affect or cognition. In the second phase of the experiment, participants rated the attitude object for the first time. In the third phase of the experiment, participants were confronted with a persuasion appeal that challenged the attitude created in the first phase.

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The persuasion appeals varied in appeal strength (strong vs. weak) as well as in framing (affective vs. cognitive). In the fourth phase of the experiment, participants’ attitudes were measured again, using the same procedure as in the second phase. The dependent variable attitude change was then assessed by calculating the difference between the first and the second attitude measurements.

Between two and five participants took part per session. At the beginning of the sessions, participants were told that the study was about the perception of magazine articles and that they were about to read magazine articles about a new product.

Manipulation of Independent Variables Participants Participants were undergraduate students of communication sciences who received credits for participating as partial fulfillment of course requirements. The sample consisted of 189 participants (131 females; Mage = 21.17, SDage = 2.25).

Materials Magazine articles specifically designed for the experiment were used as experimental stimuli. The subject of the articles was a fictitious new sunscreen called DermasolLS+, which served as the attitude object. A fictitious attitude object had to be chosen to ensure both that participants did not have preexisting attitudes, and that the induced attitudes varied predictably with regard to their informational bases. All of the articles consisted of a headline, a lead text, a picture, and the main body, and the length of the affective and cognitive articles was counterbalanced (e.g., the affective induction article was 354 words in length; its cognitive counterpart contained 349 words). Following the procedure of previous studies, positive attitudes toward the attitude object were induced in the first stage of the experiment.

In the persuasion stage, these attitudes were challenged with a counter-attitudinal appeal (e.g., Fabrigar & Petty, 1999).

In order to create the pro and contra appeals, argument valence (1 = the argument is in disfavor of DermasolLS+ to 5 = the argument is in favor of DermasolLS+) was assessed in a pretest (N = 90). For the final induction articles, only arguments that had been clearly rated as in favor of the attitude object (M > 3.5) were used, while the persuasion appeals only contained arguments that had been clearly rated as speaking against the attitude object (M < 2.5).

In sum, eight articles – two induction and six persuasion – were used for the experiment. Each participant read one of the two induction articles and either one (weak appeal) or three (strong appeal) persuasion articles (see section Manipulation of Independent Variables).

The induction articles varied in framing (affective vs. cognitive), so as to induce attitudes primarily based on either affect or cognition. In the persuasion stage, the presented articles varied in appeal strength (weak vs. strong) as well as in framing (affective vs. cognitive).

Informational Attitude Basis To manipulate the informational attitude basis, either an affective or cognitive writing style was used in the induction articles. In the affective induction article, information about the attitude object was provided using inflammatory, idiomatic, and emotional language. The affective induction article also included consumer reports, phrased as direct speech. In these consumer reports, laypersons reported on their experiences with the new sunscreen and on their emotional states when applying the product. For example, one of the persons featured in the article – a loving, caring mother of two – expressed her huge relief that, despite the frightening decline of the ozone layer, her family could go swimming and play outside without a care, thanks to this new sunscreen. The affective induction article also contained a picture of a family happily splashing around in a lake.

In the cognitive induction article, the exact same attributes of the attitude object were described, but in a dispassionate manner. Facts about the sunscreen were given impersonally, without individuals for readers to empathize with; this article also contained no emotion words or informal language. For example, the article reported the results of a clinical study that found that, in light of the decline of the ozone layer, this new product could minimize the risk of getting sunburned. The cognitive article also contained a picture of a laboratory where researchers supposedly tested the new product. However, except for the writing style and the picture provided in the articles, the affective and cognitive induction articles were identical. That is, both induction articles contained the exact same arguments. Similar approaches to inducing attitudes based on either affect or cognition were successful in previous research (e.g., Fabrigar & Petty, 1999).

Design and Procedure Framing of the Persuasion Appeals The experiment was a 2 · 2 · 2 (attitude induction [affective, cognitive] · persuasion framing [affective, cognitive] · persuasion strength [weak, strong]) factorial design. Participants were randomly assigned to the experimental conditions. The experimental sessions were held in a laboratory that provided six independent workstations.

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component: The affective persuasion articles were predominantly composed of case reports, and contained considerable direct speech and multiple emotion words, with elements such as a crying boy complaining of severe skin rashes after applying DermasolLS+. In the cognitive persuasion appeal conditions, information speaking against the new sunscreen was presented in a dispassionate, scientific tone. For example, one article reported that a study had found that 28% of people are allergic to DermasolLS+ and suffer from skin rashes after applying the product. The affective and cognitive persuasion articles also contained emotional (e.g., skin rashes) or rational images (e.g., a bar chart displaying the results of clinical tests). Again, the textual information provided in the affectively and cognitively framed stimuli was identical and only varied in terms of writing style.

In a pretest (N = 98) employing a between-subjects design, each of the stimulus articles was presented to a group of participants. After reading one of the articles, participants rated the stimulus on a scale ranging from 1 = the article is emotionally arousing to 5 = the article is rational in tone. Results revealed that the affectively framed articles’ ratings (M = 2.33, SD = 1.11) differed significantly from the cognitively framed articles’ ratings (M = 3.79, SD = 1.09), F(1, 96) = 52.90, p < .001, g2p = .31. In addition, both the affectively, t(48) = 4.26, p < .001, and cognitively framed articles’, t(48) = 5.07, p < .001, ratings differed significantly from the scale midpoint (3), indicating that our manipulation was successful.

Strength of the Persuasion Appeals The strength of the persuasion appeals was manipulated by varying both the strength and number of arguments presented. To assess argument strength, a pretest (N = 90) was conducted. Participants rated all arguments contained in the stimulus articles on 5-point Likert-type scales from 1 = not convincing to 5 = convincing. Only arguments that were rated as particularly strong (M > 3.2) in this pretest – for example, that DermasolLS+ can cause bad skin rashes – were included in the strong persuasion articles. For the weak persuasion articles, only arguments that were perceived as weakly or moderately convincing (M < 3.2) – for example, that DermasolLS+ is absorbed rather slowly by the skin – were used. Moreover, participants in the strong appeal condition groups read three affective or three cognitive articles speaking against the attitude object. These three articles were presented one after another. Some of the arguments against the attitude object were included in two or even in all of the three persuasion stimuli so as to strengthen the persuasive attempt by evoking a truth effect (Hasher, Goldstein, & Toppino, 1977). In contrast, participants in the weak appeal condition groups only read one persuasion article, which contained only the arguments that were rated as weak in the according pretest. The strong and weak arguments featured in the persuasion stimuli did not, however, directly contradict the induction stimuli. Rather, arguments against different attributes of the attitude object were presented in the persuasion articles.

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Measures Informational Attitude Basis Following the induction phase, participants completed the attitude basis measurement. Following the procedure of previous research, participants were instructed to rate the extent to which they attributed a series of eight emotional – four positive and four negative – states (e.g., satisfaction or anger) to the attitude object, using a 5-point Likert-type scale ranging from 1 = not at all to 5 = very much. The cognitive attitude component was measured by asking participants to indicate the extent to which eight rational – four positive and four negative – characteristics described the attitude object (e.g., useful or harmful) on a 5-point Likert scale ranging from 1 = totally disagree to 5 = totally agree (e.g., Crites, Fabrigar, & Petty, 1994). Separate mean scores were computed for the affective (a = .74) and cognitive (a = .78) items. Similar to previous studies, the cognitive index was subtracted from the affective index to compute an attitude basis score for participants (e.g., Fabrigar & Petty, 1999): Positive values on the resulting attitude basis index indicate attitudes primarily based on affect, negative values indicate attitudes primarily based on cognition.

Attitude Change Attitude change was operationalized as the difference between participants’ overall attitudes after reading the induction and the persuasion articles. Participants’ overall attitudes were measured using three 10-point semantic differentials (negative-positive; bad-good; undesirabledesirable; Crites et al., 1994); these attitudes were measured after attitude induction (Time 1 attitude, a = .88) and after the persuasion stage (Time 2 attitude, a = .93). The difference between the two measurement occasions was calculated by subtracting the Time 2 attitude score from the Time 1 attitude score. Hence, the higher the value on the resulting attitude change index, the more the attitude changed in the intended direction.

Processing Fluency After completing the second attitude measurement, participants completed a processing fluency measurement consisting of two semantic differentials. Participants responded to the prompt ‘‘The information presented was. . .’’ on a 5-point Likert-type scale from 1 = easy to understand to 5 = difficult to understand, as well as on a 5-point Likerttype scale from 1 = easy to process to 5 = difficult to process (Lee & Aaker, 2004).

Control Variables To rule out potential alternative explanations for the effects obtained in the experiment, two control variables were measured after the attitude induction. Attitude certainty was Social Psychology 2016; Vol. 47(1):52–62

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measured immediately after completing the attitude basis and overall attitude measurement, using a single item (‘‘How certain are you of your attitude toward DermasolLS+?’’). Participants rated their certainty on a 10-point Likert-type scale ranging from 1 = not at all to 10 = extremely certain (e.g., Clarkson et al., 2011).

As the sources of information were varied in the attitude-induction phase – the cognitive induction article referred to clinical studies, the affective induction condition featured laypersons reporting on their experiences with DermasolLS+ – the possibility that the effects found in the experiment were caused by differences in perceived source credibility had to be ruled out. Therefore, source credibility was measured using three items. Using a 5-point Likert scale ranging from 1 = totally disagree to 5 = totally agree, participants were asked to assess whether ‘‘[The persons/the study] featured in the article [were/was]. . .’’ ‘‘credible,’’ ‘‘trustworthy,’’ and ‘‘believable’’ (a = .80).1

Results Manipulation Check Time 1 attitudes were first submitted to a two-way ANOVA using the induction condition as the independent variable.

The results show that equally positive attitudes were induced in both the affective (M = 4.07, SD = 0.54) and cognitive (M = 3.96, SD = 0.49) induction conditions, F(1, 187) = 2.16, ns.

Moreover, the induction of affect- and cognition-based attitudes was successful: Participants who read the affective induction stimulus reported attitudes primarily based on affect (M = 0.17, SD = 0.92), participants in the cognitive induction condition reported attitudes primarily based on cognition (M = –0.35, SD = 0.90). The difference between the two conditions was significant, indicating that the induction of different types of attitudes was successful, F(1, 187) = 15.59, p < .001. Correlational analyses also confirmed that the attitude induction was successful: In the affective induction group, the correlation between the affective attitude component and overall attitude, r(91) = .64, p < .001, was stronger than the correlation between the cognitive attitude component and overall attitude, r(91) = .41, p < .001; z = 2.19, p = .028. In the cognitive induction condition, the cognitive attitude component correlated marginally more strongly with overall attitude, r(94) = .59, p < .001, than did the affective attitude component, r(94) = .41, p < .001; z = 1.69, p = .091.

Further testing was conducted to rule out the possibility that the induced attitudes varied in terms of attitude certainty. However, this was not the case, as participants who 1

read the affective induction article reported equally certain attitudes, M = 5.90, SD = 2.56 as did participants in the cognitive induction condition, M = 6.02, SD = 2.12; F(1, 187) = 1.03, ns. Likewise, the sources featured in the induction articles were perceived as equally credible in the affective, M = 3.88, SD = 0.72, and cognitive, M = 3.94, SD = 0.66 induction article, F(1, 187) = 0.31, ns.

Attitude Change If peripheral processes cause matching effects between message frames and informational attitude bases, one would expect matching effects for weak persuasion messages and mismatching effects for strong persuasion messages. Alternatively, if heightened message scrutiny explains the effects, one would expect mismatching effects for weak persuasion messages and matching effects for strong persuasion messages. Either way, we expected a three-way interaction between attitude induction, persuasion framing, and persuasion strength. An ANOVA using attitude change as the dependent variable and the three experimental manipulations as the independent variables revealed the anticipated three-way interaction, F(1, 181) = 15.69, p < .001, g2p = .08. Figure 1 depicts the nature of this interaction. Besides this three-way interaction, there was only one significant main effect in the ANOVA: The strong persuasion appeals (M = 2.10, SD = 0.70) were significantly more effective in changing attitudes than the weak appeals (M = 1.67, SD = 0.69; F(1, 181) = 21.63, p < .001, g2p = .11).

Our hypotheses were tested by comparing the attitude change scores of the two induction conditions (affective vs. cognitive) for each persuasion condition: affective weak, affective strong, cognitive weak, and cognitive strong. This was done using the estimated marginal means of the dependent variable (Searle, Speed, & Milliken, 1980), and this analysis revealed a significant matching effect in the weak appeal condition. Specifically, the weak cognitive appeal was more successful in changing cognition- (M = 1.89, SD = 0.78) than affect-based attitudes (M = 1.43, SD = 0.80; F(1, 181) = 5.57, p = .019, g2p = .03). This result supports Hypothesis 1a and contradicts Hypothesis 2a. The weak affective appeal was more successful against affect- (M = 1.85, SD = 0.56) than cognition-based attitudes (M = 1.44, SD = 0.47; F(1, 181) = 4.66, p = .032, g2p = .03), supporting Hypothesis 1b and rejecting Hypothesis 2b. In the strong appeal condition, a partial mismatching effect occurred: The effect of the strong cognitive appeal on affect-based attitudes (M = 2.14, SD = 0.60) was not stronger than the effect on cognitionbased attitudes (M = 1.88, SD = 0.49; F(1, 181) = 1.78, ns), thereby neither supporting Hypothesis 1c nor Hypothesis 2c. However, the strong affective appeal was

When creating the stimulus materials, a pretest (N = 98) was conducted to assess the source credibility of all of the eight articles.

Participants were asked whether ‘‘[The persons/the study] featured in the article [were/was]’’ ‘‘credible,’’ ‘‘trustworthy,’’ and ‘‘believable’’ (a = .83). Responses were given on a 5-point Likert scale ranging from 1 = totally disagree to 5 = totally agree. Results indicated that all of the sources featured in the eight articles were rated significantly higher in source credibility than the midpoint of the scale (3).

Moreover, t-tests revealed that differences in perceived source credibility between the articles were nonsignificant.

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Processing Fluency .31** (SE = .09)

.20* (SE = .08)

Experimental Condition (0 = Mismatching; -.01 (SE = .10) (.04 [SE = .12]) 1 = Matching)

Attitude Change

Figure 2. Coefficients are unstandardized; the total effect is in parentheses (*p < .05, **p < .01).

Figure 1. Attitude change as a function of attitude basis and framing of the persuasion appeal for weak appeals (A) and strong appeals (B). significantly more successful against cognition- (M = 2.40, SD = 0.61) than affect-based attitudes (M = 1.99, SD = 0.93; F(1, 181) = 4.36, p = .038, g2p = .02).

This result is in line with Hypothesis 1d, meaning that Hypothesis 2d must be rejected.

In sum, our results clearly suggest that peripheral processing accounts for matching effects between affective and cognitive message frames and informational attitude bases. This conclusion is further supported by comparisons of the time participants spent reading the persuasion appeals: In the weak affective persuasion appeal condition, participants with affect-based attitudes spent significantly less time reading the appeal (M = 79.60 s, SD = 18.00) than participants with cognition-based attitudes (M = 86.30 s, SD = 19.91; F(1, 43) = 4.22, p = .046, g2p = .09). In the weak cognitive appeal condition, the 2015 Hogrefe Publishing

amount of time spent reading the persuasion appeal did not differ between participants with cognition(M = 76.92 s, SD = 17.97) and affect-based attitudes (M = 82.26 s, SD = 18.70), despite the fact that the differences point in the expected direction, F(1, 46) = 1.01, ns.

In the strong affective persuasion appeal condition, reading time differences between participants with affective (M = 331.14 s, SD = 34.31) and cognitive attitude bases (M = 346.9 s, SD = 31.10) were marginally significant, F(1, 47) = 2.85, p = .098, g2p = .06. In the strong cognitive appeal condition, the comparison of the reading times revealed a significant difference between participants with cognition- (M = 326.22 s, SD = 30.51) and affect-based attitudes (M = 347.58 s, SD = 36.07; F(1, 45) = 4.79, p = .034, g2p = .10). These comparisons clearly support our argument that participants in the matching conditions processed the persuasive information less thoroughly than participants in the mismatching conditions.

A mediational analysis was conducted to investigate whether fluency mediates the effect of matching appeals on attitude change. We calculated a mediation model using the SPSS-PROCESS-Macro by Hayes (2013). Matching and mismatching between informational attitude basis and persuasion appeal was used as the dummy-coded independent variable (0 = mismatching; 1 = matching); processing fluency was used as the mediator, and attitude change was used as the dependent variable (see Figure 2). Moreover, strength of the persuasion appeal (0 = weak appeal; 1 = strong appeal) was added to the model as a covariate.

Results of the mediation analysis show that a match between message frame and informational attitude basis led to significantly higher processing fluency (b = .31; SE = .09; p < .01). Moreover, processing fluency had a significant influence on attitude change (b = .20; SE = .08; p = .01). The direct effect was not significant (b = –.01; SE = .10; ns), the indirect effect was (b = .06; SE = .03; 95% CI .02–.14), indicating that the influence of matching on attitude changes was fully mediated through processing fluency. The covariate of appeal strength had no effect on processing fluency (b = –.01; SE = .02; ns), but was significantly related to attitude change (b = .05; SE = .01; p < .01). These results pertaining to the strength of the persuasion appeal indicate that processing fluency mediates the effect of message matching on attitude change for strong and weak appeals. Nevertheless, mismatching is superior in the strong appeal conditions because high scrutiny of particularly strong appeals overpowers the fluency effect.

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Discussion The present study was set out to investigate the processes underlying matching effects between affective and cognitive message frames and informational attitude bases. Our results suggest that matching a message to recipients’ informational attitude bases leads to processing fluency, which in turn entails persuasion by affecting perceived message verity. If, however, particularly strong persuasion messages are presented, mismatching effects occur. This result indicates that information mismatching recipients’ informational attitude bases is processed more thoroughly than comparative matching information.

Our pattern of results stands in contrast to findings from previous studies on the processes underlying function (Petty & Wegener, 1998) and self-schema matching (Wheeler et al., 2005). These studies found that function and selfschema matching effects are driven by heightened message scrutiny. In the case of matches between informational attitude bases and message frames, this explanation is not applicable. Rather, the processes behind matching effects between message frames and informational attitude bases are the same as those accounting for the regulatory fit effect.

The results of the present paper may also provide an explanation for the moderators found in previous studies dealing with matching and mismatching effects between message frames and informational attitude bases (Ryffel et al., 2014; Clarkson et al., 2011). Clarkson and colleagues (2011) found that matching an attitude’s informational basis is a particularly successful strategy when attitude certainty is high (see also Ryffel et al., 2014). This fits well with the processing fluency explanation brought forward in the present paper, as research to date has shown that high attitude certainty is associated with peripheral processing (Tiedens & Linton, 2001), and facilitates the experience of processing fluently (Schwarz & Clore, 2007). However, the results reported by Clarkson and colleagues (2011) stand in contrast to those by Millar (1992), who found matching effects for participants with little prior experience with the attitude object and mismatching effects for participants with extensive prior experience. How is this pattern of results compatible with the conclusion that matching effects between message frames and informational attitude bases are driven by peripheral processes? If high attitude certainty really triggers peripheral processing and peripheral processes really drive matching effects between affective and cognitive message frames and informational attitude bases, one would expect matching effects for participants with extensive prior experience with the attitude object. However, previous research has indicated that confidence is associated with higher processing than is doubt when the persuasion message is framed in terms of confidence (Tormala, Rucker, & Seger, 2008). This was precisely the case in the study by Millar (1992), in which the author used riddles as attitude objects, and in which the persuasion appeals contained statements that aimed at creating confidence. The cognitive persuasion appeal indicated that the problem

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was ‘‘easy to perform’’ (Millar, 1992, p. 51), and the affective appeal was designed to foster ‘‘feelings of confidence’’ (Millar, 1992, p. 51). Therefore, participants with extensive prior experience with the attitude object might have scrutinized the persuasion messages carefully and therefore not experienced fluency; this is because ‘‘feeling confident produces thoughtful processing when information is framed in a way that matches that feeling’’ (Tormala et al., 2008, p. 145).

Limitations and Directions for Future Research Although the present paper makes a contribution to understanding how affective and cognitive appeals change attitudes, our findings should be interpreted within the study’s limitations. These are first related to our manipulation of the article tone. In order to vary the affective and cognitive tone of the stimuli, some characteristics of these stimuli had to be varied: In the affective stimuli, people were portrayed in such a way as to kindle empathy, while information contained in the cognitive stimuli information was depicted impersonally. The articles for the different conditions also contained different pictures. However, as we systematically ruled out all likely potential alternative explanations, it is unlikely that other domains that played important roles for the persuasion outcomes were affected by this manipulation.

Nevertheless, future studies should attempt to replicate our findings using different attitude objects and different sources of information to contribute to the generalizability of the effects described in the present paper.

Also, we only induced positive attitudes and changed them to negative. Thus, we can only draw conclusions regarding attitude changes from positive to negative. However, in light of the theoretical framework our work is based on, there is no reason to believe that our hypotheses are only valid for attitude changes from positive to negative.

Nevertheless, future research should further underpin the effects found in our study with empirical evidence for attitude changes in both directions.

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Fabian A. Ryffel Institute of Mass Communication and Media Research University of Zurich Andreasstr. 15 8050 Zurich Switzerland Tel. +41 44 634 46 73 E-mail f.ryffel@ipmz.uzh.ch

Received November 12, 2014 Revision received August 5, 2015 Accepted August 14, 2015 Published online December 30, 2015

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