Two players, a sender and a receiver (labeled ‘player A' and ‘player B' in the written instructions, see the Appendix, section Experimental Instructions, for an English translation of the original instructions in French) are randomly matched. The computer randomly draws a 6-sided die, and informs the sender about the outcome. The sender is then asked to choose between 6 possible messages to send to the receiver: “The outcome of the roll of die was [1, 2, .., 5, 6].” Our game replicates the ‘loaded environment' condition of Jacquemet et al. (2019). Accordingly, we explicitly label untruthful communication a “lie” and truthful communication the “truth” in the written instructions. Based on the content of the message, the receiver is asked to choose a number in the set [1, 2, 3, 4, 5, 6], which determines the payment of both subjects between two payment options, X and Y. Only the sender knows the actual payoffs generated by each option. If the number chosen by the receiver matches the die roll, both subjects are paid based on option X; otherwise, Y is implemented. This is common knowledge to all subjects.

Following Erat and Gneezy (2012), we use the combination of payoffs associated with each option as an experimental device to distinguish different types of lies. The payoffs are always set to (20;20) for the sender and the receiver if the sender's choice matches the die roll (option X). In the “selfish lie” condition, the payoffs implemented by option Y are (21;15): if the sender chooses to lie and the receiver follows the sender's message, the lie imposes a loss of 5 on the receiver, while the sender gains 1. We summarize the type of lie accordingly based on the variation in payoff induced by a lie as T[−5;1]. In the Pareto lie, by contrast, both the sender and the receiver benefit from the lie: the payoffs implemented by option Y are (30;30), and the lie is accordingly denoted T[10;10]. We facilitate inter-study comparison by purposefully selecting the values of the payoff parameters in each treatment to closely follow those used in Erat and Gneezy (2012), and Jacquemet et al. (2019). This choice leads to an asymmetry in the sender's benefit from lying. These two conditions are implemented within subjects in a random order to control for order effects. The roles are fixed, but subjects are randomly rematched with a different subject between the two conditions. To avoid the confounding effect of changes in wealth over the two repetitions of the game, only one condition is binding to determine the actual payment given to subjects at the end of the experiment. Subjects receive no additional information about the other player's decisions or payoffs until the end of the experiment.

We manipulate group identity within pairs thanks to the school in which participants currently study. The lab is located close to a leading business school, whose students represent a large share (47% as of march 2021) of the lab's subject pool. The master in management offered by this business school lies in the world top-10 according to Quacquarelli Symonds, 2020³ ranking and the school itself is part of the 2021 Financial Times top-100 business schools over the world. The experiment focuses on the lying behavior of future managers trained in this school. We always assign the role of sender to a student from this business school. In the in-group treatment (In), the receiver is also a future manager coming from the same business school. In the out-group treatment (Out), the receiver is a student from another school or university, and specialized in a discipline other than Management. These affiliations are made salient on the decision screen for subjects in both roles: once the role has been announced on the screen, a message appears informing participants that “The player A (B) with whom you will interact studies (Out: does not study) at [Name of the business school].”

Before entering the laboratory, each subject is first invited (one by one) to enter an adjacent office. The other subjects could neither hear nor see what happened in the office, as the door was always closed before the start of the procedure. In the No-oath condition while in this office, subjects randomly draw a sheet of paper from an envelope presented to them by the experimenter. The paper indicates the name of the seat they are assigned to in the lab. They are then invited to enter the lab using a side door located between the lab and the office, and the monitor invites the next subject to enter the office.

This no-oath procedure is also applied to receivers in the Oath condition. In contrast, the Senders are exposed to the truth-telling oath procedure designed by Jacquemet et al. (2013). Once they entered the office, subjects are first presented with a form untitled “Solemn oath” (see the Appendix, section English Translation of the Original Oath Form in French, for an English translation of the original form in French). They are asked to read the form and to decide “freely whether they want to sign it or not” (the experimenter follows a written script to make sure the subjects are all exposed to exactly the same procedure). The monitor makes clear to subjects that they are free to sign the form, and that neither participation to the experiment nor experimental earnings are conditional on their decision. Whatever their choice, subjects must give the form back to the experimenter, are thanked and invited to draw their seat according to the procedures implemented in the No-oath condition. To avoid communication between subjects prior to the experiment, one monitor stayed in the laboratory during the entire process and helps them find their seat in the room. Subjects receive no information about whether (i) other subjects were exposed to the oath procedure, or (ii) whether anyone else decided to sign the oath or not⁴.

A key driver of senders' behavior in our experiment rests in the potential for group-specific attitude toward lying. While senders all belong to the same group, the group of receivers in our experiment can differ by business school, which allow us to measure such heterogeneity. To that end, receivers participate to a simplified (3-sided) version of the dice under the cup task introduced by Fischbacher and Föllmi-Heusi (2013). Subjects then roll a three-sided dice available on their desk. They are told they can roll the dice as many times as they wish, but must report the outcome of the last trial. They are paid for this part according to their report: they earn 0 if they report 1, 1 if they report 2, and 2 if they report 3. Since our aim is to measure ex ante heterogeneity, this task is implemented at the start of the experiment, before the sender-receiver game. Senders are not exposed to this task; which allows us to compare their behavior to other experiments using the same sender-receiver game. At the end of the experiment, subjects are asked to fill in several questionnaires aimed at further measuring individual heterogeneity: their level of happiness (7 points Likert scale); their self-reported honesty (7 points Likert scale); the perceived honesty of other subjects (7 points Likert scale); and two measures of cognitive abilities: a 10 items version of the Raven (2008)'s progressive matrices test, and the Cognitive Reflection Test (Frederick, 2005, three reflection questions that must be answered within 60 s). This is followed by Gough (1979)'s Creative Personality Scale (a self-report personality inventory for creativity assessment), which is unrelated to the current paper. Last, we elicit the feeling of closeness to other students based on the “Inclusion of the Other in the Self” scale (IOS, a visual, 7-points, task that measures closeness thanks to the overlap between two circles introduced as representing the other and oneself; Aron et al., 1992; Gächter et al., 2015): subjects are asked about their closeness first with students from the business school and then with students not studying at the business school. The experiment ends with a socio-demographic questionnaire asking participants about their gender, their age, their level of study and the number of times they already participated to an experiment.

To implement the group identity treatment variables, subjects were invited separately to the same sessions depending on whether they registered in our subject pool database (managed using HROOT, Bock et al., 2014) as students currently enrolled in the business school or not. We have separate registration lists that allow us to distinguish the group to which subjects belong. Upon arrival, participants are called one by one by their name to check the registration information: they enter the private (oath) office at this stage. The first 10 participants whom we call all are enrolled in the business school list, and are assigned to a computer whose pre-determined role is set to sender. This allows us to control the group identity of senders in all conditions, and to implement the oath procedure on senders only in the Oath conditions.

Once in the laboratory, participants are informed about the instructions of each step of the experiment on their screen (the experiment is computerized using a software developed on Z-tree, Fischbacher, 2007). They can push a button located inside their cubicle to ask a question in private to a monitor at any point in time. All payments in the experiment are expressed in Experimental Currency Unit. The exchange rate is 1 ECU = 0.3 euros. Participants are paid a fixed fee for of 5 euros for answering the post-experimental survey, which is added to the payment that results from their decision in the payoff condition of the sender-receiver game that is randomly drawn (and the outcome from the dice-under the cup task for receivers). The average individual payoff is 12.02 euros for an average 1 h participation. We ran 13 sessions (with 260 participants, among whom 130 are senders) of the experiment at the GATE-Lab between September 2019 and February 2020. Table 1 provides the allocation of sessions and participants across the four between-subjects experimental treatments. All 63 senders who participated to an Oathsession agreed to sign the oath. This ensures the behavioral effect of the oath cannot be attributed to self-selection into compliance with the oath request.

Before moving to the results of the experiment, we use our control variables to provide an overview of the identifying variations induced by the experimental design. The first key dimension in our experiment is to compare interactions of senders with future managers to interactions with non-future managers based on the group identity treatment manipulation. Among the 160 participants who play as a receiver in the experiment, 72 are assigned to the In conditions and are not enrolled in the same business school as senders. The field of study of these Out participants make it highly unlikely they belong to the same group as participants from the target business school: 68% of them are enrolled in one of the two engineering school that are located close to the laboratory. The remaining participants study chemistry, medicine, biology, law, political science and arts. Only three participants study fields that are close to business studies: two in economics, and one in management.

In our design, the manipulation of the group identity of the receiver is instrumental and aims to reinforce the self-identity of senders as future managers. We check the internal validity of the consequences of this group assignment by comparing the answers to the two IOS questions among the senders (following, e.g., Harris et al., 2015). The results unambiguously support that perceived closeness reacts to the treatment manipulation: future managers feel closer to their fellow, with an average closeness equal to 3.96, than to subjects from the other school (3.09, the difference is highly significant, p < 0.001, according to paired-sample Wilcoxon rank sum test). This difference prevails whether senders participate to the No-oath (4.13 vs. 3.30, p < 0.001) or to the Oath condition (3.78 vs. 2.86, p < 0.001).

An important confounding effect in sender-receiver games is the possibility that lying arises as an attempt to counteract the willingness of receivers not to follow the message received (called “sophisticated deception” by Sutter, 2009). To ascertain that senders will not react to treatments because they expect receivers to react differently to their message, we check whether receivers behavior is similar between treatments. Among future managers (In condition) 75.0% of receivers decide to follow the message they receive. This proportion is slightly higher among receivers in the Out conditions, who follow the message 70.1% of the time (p = 0.678, χ² bootstrap test)⁵. We observe the same lack of difference in receivers' behavior regarding the implementation of the oath: 69.8% of receivers in Oath and 74.6% of receivers in No-oath decide to follow the message (p = 0.736, χ² bootstrap test).

In Figure 1, we provide evidence that group identity does not translate into differences in individual attitudes toward lying, based on the outcomes from the dice under the cup task performed by receivers. We plot the distribution separately within the group of future managers and non-future managers. The horizontal line in gray displays the theoretical benchmark—the uniform distribution that would result from perfectly truthful reports. Among both groups, the empirical distribution of responses clearly departs from the benchmark: the proportion of reported draws that give rise to no earnings is under-represented (p = 0.014 for future managers, p < 0.001 for other subjects; two-sided proportion test) whereas the report that pays the most is over-represented (p < 0.001 and p = 0.010; two-sided proportion test). The two almost perfectly balance, as the middle report is in line with the theoretical expectation for both groups (p = 0.430 and p = 0.607; two-sided proportion test). Importantly, lying behavior is overall similar between future managers and other subjects (p = 0.530, two-sided χ² bootstrap test). Under the assumption that receivers' behavior is representative of their group, we conclude that the behavior of senders in our experiment cannot be attributed to group-specific attitudes toward lying.

Last, our experiment incidentally provides evidence on in-group-bias in lying behavior by focusing on the No-oath conditions. We observe the induced differences in perceived identity do not translate into different lying behavior in the sender-receiver game. Irrespective of the type of lie, 56.0% of messages sent by future managers in No-oath are dishonest. We observe a small difference in the proportion of dishonest messages between the In and the Out conditions. When future managers send messages to future managers, 51.5% are dishonest as compared to 60.3%. Figure 2 provides a more detailed overview of the pattern of lying in the two conditions. Both the joint distribution of lies over the two games (p = 0.731, bootstrap χ² test) and the two marginal distributions of selfish and Pareto lies (p = 0.963 and p = 0.650; bootstrap proportion tests) are statistically no different across the two No-oath conditions.

We first look at the overall effect of the oath on lying behavior in the sender-receiver game by pooling the two (i.e., In and Out) Oath and the two No-oath conditions. Overall, offering future managers the possibility to sign a truth-telling oath decreases lying by 26.8%. Irrespective of the type of lie, the overall proportion of dishonest messages decreases from 56% in No-oath to 41% in Oath (p = 0.070, one-sided bootstrap test). Figure 3 reports the joint and marginal distributions of lying across the two sender-receiver games. The joint distribution clearly shows that the oath induces a drastic increase in the share of fully honest future managers (who send an honest message in both games): their proportion in Oath is more than three times higher (p < 0.001, one-sided bootstrap test). This increase in the share of fully honest messages is compensated by a decrease in the share of each one of the three possible patterns of lie. As a results of these sharp differences, the joint distribution is significantly different between Oath and No-oath (p = 0.004, bootstrap χ² test). The marginal distributions, displayed on the right-hand side of the figure, indicate that the oath is much more powerful on selfish lies, that happen at the expense of the receiver, than on Pareto lies, that are mutually beneficial to the sender and the receiver. The share of selfish lies is more than twice lower among subjects under oath (p = 0.012, one-sided proportion bootstrap test). The slight decrease in Pareto lies is not significant (p = 0.153, one-sided proportion bootstrap test), and such behavior remains widespread even under oath.

In Figure 4, we compare the marginal effect of the oath on lying behavior between In and Out. For each of the two, we report the joint and marginal distributions of the difference in the proportion of lies between No-oath and Oath. The marginal effect of the oath on the share of subjects who decide not to lie is very much alike in the two situations. The main difference rests in how this change is obtained. In Out, full honesty mainly results from a drastic drop in the share of full liars, whereas in In it mainly comes from a decrease in the share of subjects who decide to lie only when this behavior is selfish. This is confirmed by the comparison of the marginal distributions: the decrease in the share of Pareto lies is much higher in Out, while the marginal effect of the oath is similar on selfish lies in both conditions.

We check the robustness of our unconditional results by estimating a multinomial logit model that controls for individual covariates. The dependent variable is lying behavior as defined by the joint distribution: “no lie”, “selfish only”, “Pareto only” and “two lies”. We use honesty (“no lie”) as a reference, so that the coefficients for each of the 3 remaining outcomes can be interpreted in a natural way—a negative sign indicates a decrease in the corresponding lying behavior. We introduce treatment variables and their interactions, as well as subject's age, gender, closeness to other subjects, cognitive abilities (as measured by Raven and CRT scores) and participation to previous experiments.

The estimated parameters, presented in Table 2, confirm that the unconditional results still hold when we introduce subjects' characteristics. First, whether future managers are interacting with a fellow manager or with a student from another field of study has no effect on behavior. In contrast, we also find the oath significantly decreases all types of lying. Results also highlight that observed heterogeneity have very little predictive power on the likelihood that subjects tell a Pareto lie only, or lie in both instances. Selfish lie only stands as a notable exception: subjects who are older and performed better at the Raven test are more likely to engage into this type of lie. On the contrary, subjects who performed better at the CRT test (i.e., who override incorrect intuitive responses and engage in further reflection) are less likely to make a selfish lie only.

To sum-up, our experiment provides clear evidence that a truth-telling oath disciplines lying behavior among future managers, but only if lying is detrimental to others. When lying rather serves both the sender's and the receiver's interest, by contrast, we observe very little to no behavioral response to the oath. The obvious question raised by those results is whether lying is perceived as dishonest when it is mutually beneficial, and if yes why we do not observe the same drastic decrease as when lying is selfish.

To answer this question, we use the self-reported level of happiness collected at the end of the survey as a proxy of the internal response of subjects to the oath (see e.g., Clark, 2015, for a discussion of the internal validity of self-reported well-being as a mesaure of individual well-being). Since the level of happiness itself is difficult to interpret, we focus on variations between responses (see Jacquemet et al., 2017a, for a similar approach) and focus in Figure 5 on the level of self-reported happiness among senders who truthfully report the outcome of the dice (“truth”) and those who lie, separately by treatment. This boxplot displays the interquartile range, i.e., the distance between the upper (75th percentile) and lower (25th percentile) quartiles. Wiskers present the 10th percentile on the bottom and the90th percentile on the top end. The bold horizontal line displays the median.

Focusing on No-oath subjects, we find no change in the median level of happiness according to lying behavior in both the selfish lie (the median level of happiness among liars is 5.5 vs. 6 among truth-tellers; p = 0.280, bootstrap KS test) and the Pareto lie (6 vs. 5.5; p = 0.710, bootstrap KS test) situations. Under oath, by contrast, lying comes with a sharp shift in happiness as compared to truth-telling for both kinds of lies: the median level of happiness is lower among liars as compared to truth-tellers in the context of both selfish lies (4 vs. 5; p = 0.026, KS bootstrap test) and Pareto lies (5 vs. 6; p = 0.006, KS bootstrap test). Median happiness reaches its lowest level, equal to 3.5, among subjects who engage in both a selfish and a Pareto lie (p = 0.013 as compared to happiness among subjects who engage in Pareto lies only; KS bootstrap test)⁶. We observe a strong internal response of subjects to the oath when they decide to lie, whatever the lying situation. This response suggests that the oath makes lying psychologically more costly. The lack of behavioral response to the oath in the Pareto lie situation suggests that the benefits of a Pareto lie still outweigh the cost of lying under oath.