Signaling Resolve: Leaders, Reputations, and the Importance of Early Interactions

ABSTRACT

How do leaders develop reputations for resolve across repeated interactions? While scholars find that leaders can acquire individual reputations for resolve, we know relatively little about how these leader-specific reputations form to begin with. This article examines how leaders develop reputations for resolve from the very beginning of their tenures and present three key hypotheses regarding these leader-specific reputations. First, statements are more influential to reputational assessments during initial interactions. Second, statements create expectations of future behavior, which interact with a leader’s subsequent actions to influence reputation development. Third, initial perceptions of resolve significantly condition later assessments. Through a process tracing survey experiment, I find evidence that resolute statements are more substantively influential during early interactions. I also find early perceptions of resolve do significantly influence later perceptions. Furthermore, statements create expectations of future behavior, and it is by meeting or defying these expectations that a leader’s reputation for resolve is improved or injured within the experiment. These results remain robust even when controlling for contextual factors, including state characteristics. The implications of these findings for both scholars and policy makers are discussed, and this study illustrates how individual leaders develop these reputations for resolve across interactions.

KEYWORDS:

• Crisis bargaining
• experiment
• leaders
• reputation
• resolve

Acknowledgments

The authors thank Amanda Murdie, Thomas Preston, Steven Redd, Wesley Renfro, James Scott, and the anonymous reviewers at International Interactions for their thoughtful comments and feedback.

Funding

The authors thank the Bradley Foundation and the Duke Program for the Study of Democracy, Institutions, and Political Economy for providing funding for this research.

Supplemental data

Supplemental data for this article can be accessed on the publisher’s website.

Notes

¹ I, therefore, do not examine where reputation adheres.

² See Colaresi 2004b.

³ Deterrence theorists have long suggested individual leaders acquire these reputations (Huth 1997; Jervis 1976); yet, this line of inquiry has only recently been undertaken.

⁴ A rich literature also demonstrates leaders are critical to the conduct of international security (see Byman and Pollack 2001; Chiozza and Goemans 2011; Horowitz, Stam, and Ellis 2015; Jervis 1976; Saunders 2011).

⁵ Uncertainty and threat also increase domestic incentives for leaders to employ hawkish rhetoric (Colaresi 2004a).

⁶ Kennedy’s credibility was also undermined by his irresolute action.

⁷ This strategy could make leaders more vulnerable to threats initially.

⁸ I also examine the effect of regime type, but it is insignificant across my analyses.

⁹ Factorial experiments use scenarios with varying factors to directly compare treatment effects (Auspurg and Hinz 2015: 4).

¹⁰ Process-tracing experiments can investigate foreign policy decision-making specifically (Astorino-Courtois 2000; Mintz et al. 2006).

¹¹ Focusing on a single issue improves clarity for participants. I directly test for reputation development, rather than reputation transferability across challengers/issues. One could argue this is a most likely case for leaders to develop reputations for resolve. Future scholarship should consider how reputations form across different disputes/issues.

¹² Control questions are taken from Tomz (2007) with permission.

¹³ I exclude participants who incorrectly answer two factual questions about the scenarios (Paolacci, Chandler, and Ipeirotis 2010).

¹⁴ While real world crises progress over weeks/months/years, panel studies, which engage the same participants across time, often have high drop out rates, exacerbating problems of external and internal validity.

¹⁵ I am careful to ensure the scenario wording does not bias participants’ assessments. Participants assigned to irresolute leader treatments, for example, are told the summit ended before a final compromise was arranged. Participants assigned to resolute leader treatments are told it “was clear a compromise could not be reached.” Participants assigned to state information only groups do not receive information about leader resolve in the scenario. In revealing information about the leader’s type during information selection, I employ statements suggesting the leader prefers compromise to make the scenario more realistic. The alternative would be to use no statements to signal a lack of resolve. However, there are only 4 out of 1037 instances in the actor-level ICB dataset where an actor failed to respond to a threat. The experiment uses straightforward statements to clearly communicate the leader’s type to participants. Future research should examine whether more subtle verbal cues communicate resolve.

¹⁶ Participants are not told which treatment group they are assigned to or the type of information other participants can access.

¹⁷ Participants are told accessing information would cost them $0.01 and a correct assessment would yield an additional bonus. However, participants were not penalized for accessing information, and all participants received the bonus. This deception mimics the real world trade-off between making good assessments and the costs to make these decisions. Robustness tests with a smaller sample reveal this deception does not affect how participants access information.

¹⁸ In the vernacular, resolve means to compromise, the opposite of how it is used in the literature.

¹⁹ I find no significant difference between the combined measure and individual measures (as a dependent variable) or between each individual measure.

²⁰ This information is presented as a leader’s statements regarding state interest. I chose not to use domestic public opinion, as this could lead participants to conclusions about regime type. I do not believe this decision muddles the relative impact of statements of leader resolve versus information about state interest, as information regarding state interest does not make claims regarding the toughness of the leader’s action. Alternative pre-tested surveys directly told participants the state had a high or low interest in the dispute, but debriefing discussions with participants indicated they viewed this as unrealistic. Future research could repeat the experiment using alternative ways of revealing state interest.

²¹ Amazon Mechanical Turk participants are less subject to experimenter bias, increasing internal validity (Paolacci et al. 2010).

²² This is comparable the finding that ~80% of world leaders have at least some college education (Horowitz et al. 2015).

²³ It would be inappropriate to include participants who did not access a given treatment in the analyses. This could be viewed as a limitation, as participants may be predisposed to only access information central to their decision-making, leading to a significant outcome. I do not find this to be the case, as, even though participants believe information is important to their decision-making and access that information, not all of this information has a significant effect on their assessments. Participants access different types of information at comparable rates throughout the experiment, indicating there is not a predisposed bias toward leader-specific or state-based information.

²⁴ Online appendix Table S1.

²⁵ These participants can only access one type of state-based information throughout the experiment.

²⁶ Full results in online appendix Table S2 through Table S4.

²⁷ No participant assigned to the weaker condition chose to access only this information during the crisis stage.

²⁸ As the dependent variable is ordinal, I employ OLS rather than logit. Full results in online appendix Table S5.

²⁹ Online appendix Table S6 through Table S13.

³⁰ Online appendix Table S16 and Table S17.

³¹ A minimum effect size of |0.8| is the standard to demonstrate a large substantive effect.

³² Relative effect size during summit vs. negotiations: d = 0.145; 95% CI: −0.017, 0.307; relative effect size during summit vs. crisis: d = 0.157; 95% CI: −0.024, 0.338.

³³ Online appendix Table S18.

³⁴ Resolute leader statements have a comparable effect size to a leader’s behavior during both the negotiations (d = −0.061; 95% CI: −0.236, 0.115) and the crisis (d = −0.019; 95% CI: −0.211, 0.173). Irresolute statements are comparable in their effect size to irresolute behavior during both negotiations (d = 0.064; 95% CI: −0.107, 0.236) and the crisis (d = 0.157; 95% CI: −0.030, 0.343).

³⁵ Full results in online appendix Table S19.

³⁶ If assessments of resolve are based solely on behavior, there should be little difference across treatment groups where the leader ultimately behaved resolutely (or irresolutely).

³⁷ Participants receiving the Resolute/Resolute/Irresolute condition (M = 2.662, SD = 0.911), for example, predict the leader will be as tough and determined as participants receiving either the Resolute/Irresolute/Irresolute (M = 2.282, SD = 0.912; F[1,87] = 3.65, p = .059) or Irresolute/Resolute/Irresolute condition (M = 2.340, SD=0.823; F[1,82] = 2.84, p = .096).

³⁸ The previous set of analyses shows that, when participants receive contradictory information about leader resolve, their perceptions of resolve are influenced by earlier information. This suggests my results regarding the impact of initial perceptions on later perceptions are not simply due to participants holding consistent impressions of resolve regardless of a leader’s signals.

³⁹ Online appendix Table S20.

⁴⁰ The 95% confidence intervals on some variables are so narrow that they are not visible on the graph.

⁴¹ Online appendix Table S21 through Table S23.

Additional information

Funding

The authors thank the Bradley Foundation and the Duke Program for the Study of Democracy, Institutions, and Political Economy for providing funding for this research.