Trust, Truth, Status and Identity: An Experimental Inquiry

However, there are a few important counter-examples and negative findings. In terms of counter-examples, McLeish and Oxoby (2008) find that individuals are more likely to levy costly punishment on in-group members for bad behavior than on out-group members, which seems inconsistent with treating in-group members better but is consistent with an evolutionary group-selection model for the existence of social norms (Bernhard, Fischbacher, and Fehr 2006). In terms of negative results, several studies find no effect of equal-but-different groups at all: Güth, Levatti, and Ploner (2008), as well many of the treatments in Charness, Rigotti, and Rustichini (2007) and Eckel and Grossman (2005).

The World Values Survey asks how justifiable such morally wrong behaviors as cheating on taxes or unjustly claiming government benefits are. Respondents answer on a scale from 1 (never justifiable) to 10 (always justifiable). The authors find that respondents who view themselves as belonging to a higher social class tend to rate these behaviors as less frequently justifiable.

This pattern is also consistent with the classical in-group bias results in the context of disinterested money division tasks, particularly if in-group bias is the norm (Harris, Herrmann, and Kontoleon 2010; Hertel and Kerr 2001; Jetten et al. 1997).

Two relevant examples: (i) “From everyone who has been given much, much will be demanded; and from the one who has been entrusted with much, much more will be asked.” Luke 12:48; (ii) “Not many of you should become teachers, my fellow believers, because you know that we who teach will be judged more strictly.” James 3:1.

Peter Parker’s uncle, in Stan Lee’s Spiderman, famously advises: “With great power comes great responsibility.”

The experimental literature in social psychology starts with Tajfel et al. (1971). See Mullen, Brown, and Smith (1992) or the references and discussion in Chen and Li (2009) for a nice overview of subsequent psychological research.

Also many of the treatments in Charness, Rigotti, and Rustichini (2007) and Eckel and Grossman (2005) yielded no significant evidence of in-group bias.

This phenomenon could also rationalize a wide array of seemingly unrelated or contradictory results concerning the effects of status in the experimental economics literature. For example, the hypothesis is consistent with the results in Ball et al. (2001) where prices in two-sided auctions favor high status experimental participants, if profit-maximization is the norm that governs that situation. It is also consistent with increased giving by high status players in public goods games (Kumru and Vesterlund 2008).

The refreshments were modest, consisting of a glass of water or lemonade as well as some snacks – crackers, cheese and grapes.

By reinforcing the random status assignment, I follow previous experimental work on status in the laboratory. For example, in Ball et al. (2001) a random status assignment was reinforced and made more salient by having low status participants clap for high status participants.

The number of rounds varied across sessions because of time constraints.

Even though participants were seated by color group, there were several people (8–10) in each color group in each session making the assumption of anonymity still plausible.

This differs slightly from the trust game in Berg, Dickhaut, and McCabe (1995), where both senders and receivers were endowed with $10.

The descriptive terms used here (reliable, lemon, buyer and seller) and later in the analysis of the truth game are for expositional purposes only. The state space and message space were actually {Heads, Tails}, each buyer’s action set was {Left, Right} and players were called “senders” and “receivers.” See the Appendix for experimental instructions.

Other equilibria are possible, including a perverse equilibrium in which the buyer believes the car is reliable whenever observing the message “lemon.” I discuss this equilibrium in the Appendix.

Relaxing this last assumption makes the algebra slightly messier and implies some lying even when the seller knows the car is reliable but adds little intuition.

Since money sent was tripled, the proportion returned can take values from 0 to 3. Excluded are observations where nothing was sent where the return ratio $Returned$Sent is undefined.

These similarities are striking given the differences in initial endowments in the current design not present in the original trust game experiments, already suggesting that distributional preferences alone cannot explain participant behavior.

Specifically, the marginal impact of a dollar sent on the average return ratio was 0.043 for low status receivers, while it was 0.043 + 0.106 = 0.149 for high status receivers – more than three times as large. Furthermore, in all but the least elaborate specification (column 1) the estimated marginal impact of one additional dollar sent on low status receivers’ return ratios is not significantly different from zero, indicating a strikingly weak concern for reciprocity on the part of low status receivers.

The following robustness checks were conducted (not reported, but available upon request): (i) including individual receiver random effects; (ii) clustering standard errors at the individual level rather than the session level; (iii) accounting for censoring using Tobit instead of OLS. In all of these alternate specifications: (i) high status receivers are significantly more reciprocal than low status receivers and (ii) senders’ group affiliation did not matter for behavior.

It might seem more natural to explain variation in behavior with individual heterogeneity in the weights placed on identity utility, αj, and ideals that do not vary by identity category. However, with this approach, it is difficult to simultaneously explain why high status receivers are less generous when sent a low amount and more generous when sent a high amount – a result that obtains below.

Censoring from above is also possible, but not quite as worrying as there are very few observations in the data where the maximum possible amount was returned.

The main error-term assumption required for CLAD to be consistent is that errors have median zero, which is quite a bit less restrictive than the standard assumption of normality and homoskedasticity. The tradeoff is that an assumption must be made about the data. Roughly speaking, there must be “enough” uncensored observations which is likely to be satisfied in the present case.

Individual random effects are used to take into account the fact that we have repeated observations on individuals where in some observations the individual is part of an in-group pairing and in some other observations the same individual is involved in an out-group pairing.

The regressions for the S-ID data roughly correspond to Table 3, column 1, as they do not control for sender status. The figure therefore represents a conservative estimate of how return ratio function slopes vary by status.

Of course, agent j’s ideal could also depend on her co-player’s social category, but since there was no evidence of this in the S-ID version of the experiment, this possibility is not modeled.

It looks rather out of place, but the 4 in α˜ is an artifact of factoring –2 out of (4s−2r−7) to get the expression in the parentheses into an r−rIdeal(s) format. This is also where the 7/2 term in rIdeal comes from.

For direct supporting evidence on this point in the context of a dictator game with third-party punishment, see Butler, Conzo, and Leroch (2013).

The actual average difference in the data is $1.53. This does not necessarily imply that my model organizes the data poorly, however. The observed discrepancy between the model prediction and the data may result from several factors: senders’ ideals may vary by status, which I assume away for simplicity here; alternatively, αj may have a group-contingent component, which I again have assumed away for simplicity. For example, the pattern is consistent with low status receivers generally placing less weight on identity (α¯L<α¯H).

There is an important subset of economists who argue that the trust game has nothing to do with trust. Addressing this meta-critique of the trust game is beyond the scope of the current inquiry, but direct evidence that the trust game does involve trust is provided in Butler, Giuliano, and Guiso (2012).

This is not true for receivers, of course, because each round a receiver faces a potentially different choice: how much to return conditional on being sent x dollars, x=0,…,7. Therefore, the simpler route of constructing one average reciprocity measure for each individual receiver would be problematic.

On average, high status senders sent $4.26, while low status senders sent $3.47. Using a one-tailed t-test the difference is significant at the 5% level (p = 0.042). Regressing individuals’ average send amounts on a dummy for high status senders yields a marginally significant difference (p = 0.064). Both of these tests involve 84 observations – one for each S-ID participant. The OLS regression uses robust standard errors clustered by session.

Again, these numbers are calculated using one (summary) observation per individual, for a total of 84 observations.

The increased trust exhibited by high status S-ID senders in the raw data is slightly smaller, at 22%, but still considerably larger than in-group bias in ID-only sessions.

That is to say, this dummy variable takes the value of 1 when the seller’s message matches his or her private information and 0 otherwise.

This equilibrium arises when buyers always believe the opposite of the message sent. Given these “incredulous” buyers, sellers pool on sending the message “lemon” irrespective of their private information, so that sellers lie about good information and tell the truth about bad information.

I thank an anonymous referee for suggesting this comparison, generally, and this efficiency measure specifically.

As an example, consider an interaction in which the trust game sender sends 3. The total earnings of both players would be 7 + 2* 3 = 13 since each dollar sent creates two extra dollars in surplus. Maximum total earnings occurs when the sender sends as much as possible, i.e. 7, yielding total earnings of 7 + 2* 7 = 21. The minimum possible total earnings (7) occurs when the sender sends 0. Thus, the efficiency of an interaction where a sender sends 3 is 13−721−7≈0.43.

Pushing this intuition a bit further, if the proposed wealth effect resulted in an approximately uniform increase in generosity, we should see “wealthier participants” return a fixed amount more to their co-player for each amount initially sent than their poorer counterparts. Since this constant extra generosity would have greater impact on return ratios for low return amounts, this uniform extra generosity should imply flatter return ratio functions for high status/wealthier participants. This was exactly the opposite of the observed patterns.

A gift-exchange game is similar to the trust game. There are two players. One player moves first and chooses how much of a fixed sum of money to transfer to his or her co-player – player 2. Player 2 observes the amount transferred and decides how much “effort” to exert. Effort decreases player 2’s earnings but increases player 1’s earnings. Reciprocity is measured as the responsiveness of the effort decision to the transfer decision. Generosity is measured by the amount of effort exerted when the initial transfer is zero.

They also mirror, by the way, the hypothetically “wealthier” participants outlined above.