3.1. Do people engage in TPP?

In an early experiment on TPP (Kahneman, Knetsch, & Thaler, 1986), participants endured a cost 74% of the time to reduce the payment of participants who chose an uneven split (i.e., were “unfair”) in a Dictator Game. However, punishing unfair players and rewarding fair players were confounded in this study. Subsequently, Turillo, Folger, Lavelle, Umphress, and Gee (2002) removed this confound and found that only 15% of their participants punished unfair players—a proportion not significantly different from the proportion of individuals who punished fair players (see also Ottone, 2004).

Most closely related to the studies reported here, Fehr and Fischbacher (2004) examined TPP in the context of one-shot Dictator Game and Prisoner's Dilemma Game. In the TPP dictator experiment, Player A transferred 0–100 points (in increments of 10) to Player B. An uninvolved Player C indicated, for every level of Player A's transfer, how much of their 50-point endowment they would spend to reduce Player A's payoff, each point resulting in a three-point reduction. More than 60% (14 of 22) of participants were willing to pay to punish. When dictators transferred nothing, third parties spent an average of 14 points (28% of their endowment) on punishment, although dictators nonetheless profited from selfishness. In the analogous Prisoner's Dilemma Game, defectors were punished most severely when the defector's counterpart cooperated. In this case, 46% (11 of 24) of third parties punished defectors, and the overall average expenditure on punishment was 3.35 points (8.4% of endowment).2

TPP has also been investigated in the context of public goods games (Ledyard, 1995) in which people in one group are able to inflict costs on members of another group. Carpenter and Matthews (2005) found that only 10% of participants punished individuals in a group different from their own, and the overall amount spent to punish individuals in a different group was about US$0.10—a small amount given the average earnings of US$16 (net of show-up payment) per participant.

In sum, the TPP documented in previous studies ranged in magnitude from negligible to modest. Questions remain, however, about the role of anonymity.

3.2. Cues to social presence in economic games

The effect of the presence of others has a long and distinguished history in social psychology, dating back at least as far as early work on “social facilitation” (Zajonc, 1965; see also Triplett, 1898). Effects of observation are influenced by task difficulty (Markus, 1978), the extent to which one's performance is being evaluated (Cottrell, Wack, Sekerak, & Rittle, 1996), and details about the observer (Butler & Baumeister, 1998). The presence of others has long been known to have effects on decisions to engage in more prosocial (Latane, 1970), and less antisocial (Diener, Fraser, Beaman, & Kelem, 1976), behavior, consistent with the view that people are concerned about others' perceptions of them, especially in the domain of morality (Jones & Pittman, 1982).

Of particular relevance, Hoffman, McCabe, Shachat, and Smith (1994) found that, in a Dictator Game, when participants were assured that the experimenter would not know how much money they chose to transfer, the majority of participants gave $0, less than what is typically found in such games (e.g., Forsythe, Horowitz, Savin, & Sefton, 1994). Furthermore, as predicted by modular approaches, cues that one is being observed increase prosocial behavior, even in the absence of actual observation (Kurzban, 1998; for a recent extended discussion of modularity, see Barrett & Kurzban, in press). Kurzban (2001), for example, showed that, in a public goods game, having people exchange mutual oblique eye gazes (but no information about others' contributions) increased contributions to the public good in (all-male) groups compared to a control condition with no eye gaze. Haley and Fessler (2005) and Burnham and Hare (in press) have shown similar effects of cues to social presence, respectively, in a Dictator Game and in a Public Goods Game.

5.1. Method

5.2. Results

Overall, DM1s chose not to trust DM2 in 60% (21 of 35) of cases. Conditional on DM1 moving down, DM2s chose the uneven outcome in 64% (9 of 14) of cases. When the payoffs (DM1, DM2) were (US$1, US$39), (US$3, US$37), and (US$6, US$34), only one of seven DM1s moved down (“trusted”); in each case, DM2 chose the uneven split. When the payoffs were (US$9, US$31), four of seven DM1s “trusted,” and only one DM2 proved to be trustworthy. When the payoffs were (US$12, US$28), six of seven DM1s trusted, and three DM2s proved to be trustworthy. These results are peripheral to our method. The single trusting move by one DM1 when the payoffs were (US$1, US$39), with the subsequent untrustworthy move by DM2, generated the stimulus object needed for the subsequent punishment round.

Central to our hypotheses is the behavior of participants in the sessions in which DM2s could be punished (Fig. 1).6 In the punishment round, 38% (9 of 24) of third-party participants paid to punish in the Anonymous condition, while 47% (9 of 19) punished in the Experimenter condition. Because of the skewed distribution and because we had a directional prediction, we conducted a one-tailed Wilcoxon rank-sum test (z=1.52, p=.06), obtaining a result just shy of standard levels of significance. We therefore conducted an additional analysis that retains some of the information lost in the Wilcoxon test. We treated punishment as a binary variable, categorizing each punishment decision as either less than half of the endowment (US$0–3) or greater than half of the endowment (US$4–7). Using this test, the difference between the two conditions is statistically significant (p=.002, Fisher's Exact Test). This result is still significant after a Bonferroni correction for all six possible divisions between zero and seven (adjusted α=.05/6=.008).

Fig. 1. Distribution of punishment decisions in Experiment 1. (The outlier has been omitted; see footnote 6.)

5.3. Discussion

People punished more when their decision would be known to the experimenter than under conditions of anonymity. This result is consistent with reputation-based accounts of moralistic punishment.

The Trust Game, however, might not be the best means of eliciting a “norm violation.” Indeed, researchers in the behavioral economics literature differ on the interpretation of decisions in the Trust Game (see, e.g., Cox, 2004, Cox & Deck, 2005), and it is not clear that our participants uniformly construed DM2's move to the right as untrustworthy. This raises questions about both the use of the Anonymous condition as an index of a taste for punishment and the use of the Treatment condition as an index of a desire for a positive reputation. In Experiment 2, we used a sequential Prisoner's Dilemma Game to obtain less ambiguous norm violations.

6.1. Method

6.2. Results

In the sequential Prisoner's Dilemma Game, (Cooperate, Cooperate), (Cooperate, Defect), (Defect, Cooperate), and (Defect, Defect) occurred 6, 8, 10, and 16 times, respectively. The relatively high frequency of (Defect, Cooperate) is extremely unusual, a result for which we have no good explanation. It is, however, irrelevant to the present study, as the Prisoner's Dilemma Game was used only to generate a Cooperate–Defect sequence of moves.

The proportion of participants who engaged in costly punishment in the Anonymous, Experimenter, and Participants conditions was 42% (13 of 31), 65% (17 of 26), and 67% (20 of 30), respectively. The mean (S.D.) expenditure on punishment was US$1.06 (1.65), US$2.54 (2.70), and US$3.17 (3.60), respectively (Fig. 3).

Fig. 3. Punishment decisions in Experiment 2. Error bars are 1 S.E. The full scale is not shown. The total punishment possible is US$10.

Again because of the distribution of the data, we conducted a nonparametric Kruskal–Wallis rank-sum test, finding that money spent on punishment differed across conditions [χ2(2, N=87)=7.56, p=.02]. We further conducted pairwise Wilcoxon rank-sum tests, which showed that more money was spent on punishment in the Experimenter condition than in the Anonymous condition (z=2.25, p=.02), and that more money was spent on punishment in the Participants condition than in the Anonymous condition (z=2.47, p=.01). Punishment did not differ significantly between the Experimenter and Participants conditions (z=.33, p=.74). Selfish individuals gained US$5 by defecting, while they incurred average punishments of US$3.18, US$7.62, and US$9.51 in the Anonymous, Experimenter, and Participants conditions, respectively.

Three independent raters scored participants' comments explaining their decision on a scale from 1 to 7. Raters were asked to indicate “how [X] the person making comments seems to be,” where X=angry, disgusted, contemptuous, guilty, ashamed, and selfish. Because Cronbach's α (a measure of interrater agreement) values for guilty and ashamed were only .69 and .67, respectively, we omitted these results (see Table 1).

Table 1. Experiment 2: reliability and mean ratings (S.D.) of free responses

	Scale	Cronbach's α	Condition
			Anonymous	Experimenter	Participants
	Angry	.89	1.86 (0.70)a	2.45 (1.45)b	2.39 (1.26)b
	Disgusted	.87	1.88 (0.75)a	2.28 (1.34)a,b	2.47 (1.38)b
	Contemptuous	.89	1.98 (0.77)a	2.53 (1.38)a,b	2.64 (1.37)b
	Selfish	.88	4.83 (1.20)a	3.97 (1.70)a,b	3.46 (1.31)b

Ratings are on a scale from 1 to 7 (see text). Within each row, entries that do not share a superscript differ at p<.05. For “selfish,” the difference between Anonymous and Participants is significant at p<.0001. Because we predicted greater emotion in the Experimenter and Participants conditions, and greater selfishness in the Anonymous condition, all tests are one-tailed.

6.3. Discussion

Under conditions of anonymity, participants punished someone who defected after a cooperative move in a sequential Prisoner's Dilemma Game, but this punishment was small—roughly US$1 or 10% of the possible amount they could punish. Knowledge that the experimenter, or the experimenter and other participants were going to know how much an individual punished increased this amount—more than tripling it in the latter case.

Quite unexpectedly, in the Participants condition, at least one subject attempted to deceive others by announcing a false outcome. Because we did not anticipate deception, we did not record this information and could not determine the relationship between dissembling and punishment decisions. We suspect, but could not confirm, that those who punished the least were most likely to attempt deception. The fact that we observed dissembling testifies to the importance of computations regarding reputation.

7.1. Situating the results

The implications of our results for evaluating relevant theory can be seen most clearly in the context of work on the effect of anonymity in a slightly modified version of the Ultimatum Game. Bolton and Zwick (1995) used a set of extensive-form games in which the first decision maker could choose to allow the second decision maker to select between one of two options: (a) US$2 for each or US$0 for each, or (2) an unequal split (benefiting DM1) of US$4 (e.g., US$3.40/US$0.60) and US$0 for each. In the latter case, the choice of US$0 for each is interpretable as a punishment for DM1 choosing to forgo the possibility of evenly splitting the US$4 endowment. In a condition analogous to our anonymity treatment, in which DM2's decisions were unknowable by the experimenter, anonymous punishment of uneven splitters was very similar to the control condition [see especially Figs. 5 and 6 (pp. 110 and 111, respectively) of Bolton & Zwick, 1995], Bolton and Zwick conclude that the effect of being observed by an experimenter is “relatively weak” (p. 113) compared to the “propensity to punish those who treat them ‘unfairly,’ independent of any influence exerted by the experimenter” (p. 96).

These results, combined with those from the present study, suggest that anonymity has a weaker effect in the context of second-party punishment than in the context of TPP. This speaks to the question of the nature of psychological design and the ultimate explanation for these different types of punishment. Put simply, these results raise the possibility that punishing someone who has treated you unfairly is a taste that can override the taste for individual gain or wealth, and is not substantially mediated by cues that one is being observed. In contrast, the taste for TPP is weak compared to the taste for individual gain, and is mediated by cues that one is being observed.

Bridging from these results to ultimate explanations must necessarily be tentative. However, this contrast hints that adaptations for second-party punishment might have been driven by selection pressures associated with repeat interactions with particular individuals (Trivers, 1971). In contrast, adaptations for TPP might have been driven, at least in part, by selection pressures associated with reputation, as suggested by sensitivity to observation. The small amount of TPP under conditions of anonymity is subject to a wide variety of interpretations, including “mismatch” explanations (Hagen & Hammerstein, 2006) and the models described above (e.g., Gintis, 2000). Future work will need to clarify the design features associated with both types of punishment. The current data raise the possibility of different histories of selection for the computational systems that underpin these two types of punishment, and that they might be, to some extent, functionally distinct.

7.2. Are demand characteristics an alternative explanation?

Demand characteristics refer to features of an experiment that allow participants to infer what is expected of them and thereby cause them to act in that way, limiting the inferences that can be drawn from the experiment (Orne, 1962). Experiments with financial incentives contingent on participants' decisions minimize this problem because decisions have genuine consequences, as opposed to participation in exchange for a fixed payment or course credit (Hertwig & Ortmann, 2001). In any case, it is worth addressing this concern very carefully as our experiment is unusual in this regard.

Two points must be kept firmly in mind. First, the only mechanism by which experimenter demand can cause differences is by virtue of differences among Treatment conditions. Second, participants in the Anonymous conditions knew that the experimenters would be collecting the data from the envelopes in the bin. Thus, Treatment conditions did not differ insofar as participants expected that the experimenters would eventually know people's choices, whether individually or in aggregate.

One possibility is that the instructions in the nonanonymous conditions caused participants to be concerned about appearing appropriately punitive, causing them to punish more. If so, demand characteristics are not an alternative explanation because this was the point of manipulation. Our interest was in the effect of concern for what others know about one's behavior in the context of moralistic punishment.

If we suppose the operation of the traditional construal of experimenter demand—that participants were motivated to generate data that conform to the predicted effect—then we must ask a great deal of our participants. Because it was a between-participants design, participants would have to: (a) correctly guess what was being varied across conditions; (b) correctly guess how much people in the other condition punished; (c) correctly guess our directional prediction; and (d) choose to punish an amount that conformed to (a)–(c), ignoring other motives (financial or reputational). While this is not impossible, concern for one's reputation is much more plausible.

7.3. Future directions

These results lead to a number of questions to be addressed in future research. First, what specific reputational benefits are gained by being perceived as a third-party punisher? By analyzing people's judgments of punishers and nonpunishers, we hope to understand the reputational gains from moralistic punishment. Second, arguments regarding the putatively modular system underlying punishment suggest that mere cues of social presence, such as eyespots, might exert effects similar to those of actual social presence (e.g., Haley & Fessler, 2005). Determining the conditions that elicit greater punishment can provide insight into the nature of the inputs that activate this computational system.

Other important routes of investigation include: (a) determining the role of intentions, which will help to shed light on models based on avoiding inequities (e.g., Fehr & Schmidt, 1999); (b) determining the role of emotions, which are receiving increasing attention in economic decision making (Fehr & Gächter, 2002, Frank, 1988); and (c) determining the specificity of the effect observed in these experiments–do similar effects occur in the context of other norm violations, or is there something special about the interactions investigated here? These lines of research should help illuminate the cognitive adaptations responsible for moralistic punishment.