Is there a link between endowment inequality and deception? - an analysis of students and chess players.

This paper investigates experimentally the relationship between inequality in endowment and deception. Our basic design is adopted from Gneezy (2005): two players interact in a deception game. It is common knowledge that player 1 has private information about the payoffs for both players of two alternative actions. Player 1 sends a message to player 2, indicating which alternative putatively will end up in a higher payoff for player 2. The message, which can either be true or false, does not affect the payoffs of the players. Player 2 has no information about the payoffs. However, player 2 selects one of the two alternatives A or B, which is payoff-relevant for both players. Our paper adds value to the literature by extending Gneezy (2005) in two ways. First, we systematically vary the initial endowment of players 1 and 2 (common knowledge to both of them). Second, we do not limit ourselves to the standard population of university students but also recruit chess players that are not enrolled in any degree program. Doing so, we want to find out if our results remain robust over a non-standard subject population which is known to be experienced to some extent in strategic interactions. Our main findings are: (i) non-students behave more honestly than students, (ii) students are more likely to trust the opponent's message, and (iii) students and non-students behave differently to variation in initial endowment.

1. Introduction

Inequality can be found in most areas of life. Examples include the allocation of natural resources such as water and oil around the world. Material inequality is particularly widespread: global wealth is concentrated in the hands of a small number of people ([1, 2]). Inequality is often the starting point for conflicts in society (e.g. between different religions, gender wage gap, etc.). What are the behavioral foundations of inequality from a microeconomic point of view?

Episodic evidence suggests that the spectrum is multifaceted. Some people ignore poor people, others anonymously donate large amounts of money. Some people look up to rich people, while others become envious. While it is still mainstream to model individuals to derive utility exclusively from their own consumption, economists are increasingly recognizing that people are not only interested in their absolute but also in their relative position of wealth ([3]). There is a bunch of evidence that people compare themselves with others (e.g. [4-7]). In their model [8], assume that people are not only interested in their monetary payoffs (as purely selfish individuals would be) but also care about its distribution. They are supposed to dislike inequitable outcomes. Inequitable outcomes can arise both when individuals have less and when they do have more than others.

In their meta-analysis about experimental studies in economics, psychology, and sociology [9], find that people often refrain from telling lies. Our paper investigates the link between deception and inequality. In this realm, the question arises of whether people are more inclined to lie to poorer or richer individuals. Several authors have tackled this field of research recently. For example [10], find in their experimental studies a link between monetary incentives and upward social comparisons: people tend to cheat more if they know that close others earn more. Similarly [11], find experimental evidence for dishonest behavior if subjects are relatively disadvantaged in groups [12]. Link honest and dishonest behaviors to financial self-interest and equity concerns [13]. Analyze experimentally the norm that “one gets what one deserves” on honesty in a design where dishonesty entails income redistribution. The authors find a link between norm violation and the propensity toward dishonesty.

The subject of lying is a sensitive one, which complicates analyzing it. There are several possible ways to investigate the association between inequality and deception. This includes real data. For example [14], are investigating the distribution of true and false online messages on Twitter. The tendency to lie can also be examined with the help of questionnaires. The randomized response technique is well established in the literature for sensitive questions. However, we resort to economic experiments. Controlled experiments allow us to draw causal inferences. To study lying to other people (instead of lying to yourself in which the die experiment or a real effort task are quite common; e.g. [15, 16]), our paper adopts the basic design of [17]’s (2005) two-player cheap talk sender-receiver game. Player 1 has two options A and B. She is fully informed of the monetary consequences for herself and the opponent. Player 1 sends a message to player 2, indicating which of the two options is supposedly financially advantageous for player 2. This message can be honest or a lie. Player 2 remains uninformed about the monetary consequences associated with the payoffs. However, player 2 knows the message sent by player 1, and picks one of the two options which eventually will be played out (i.e., payoff-relevant) for both players. To analyze the link between inequality and deception, we extend the basic design of [17] to systematic variations in initial endowment. The topic of inequality has been tackled in the experimental literature with mixed findings. For example, in the realm of trust games [18], found evidence for inequality to matter, whereas [19] does not find evidence for inequality aversion. In our extended [17] design, we provide either player 1 or 2 with an initial endowment of €10 in the treatment conditions. In accordance with [8], we distinguish between monetary advantageous inequality and monetary disadvantageous inequality.

Unlike most experimental studies, we do not only recruit students as subjects. Students are readily available, which makes their recruitment relatively easy. They have low opportunity costs and steep learning curves. The latter is partly due to training in solving abstract problems ([20, 21]). In contrast, recruiting non-students often poses a challenge because of their higher opportunity costs. On average, they are older and therefore have more job experience. The many differences between students and non-students raise the question of the external validity of experimental studies with students: What can we reasonably learn from experimental studies with students if we are interested in the decision behavior of non-students? There is only a limited number of studies that systematically compare students and non-students. According to [22], non-students behave as if they were more pro-social oriented. However, based on a literature review of 13 papers [23, 24], found no systematic, qualitative behavioral differences between students and non-students. Differences are attributed to the gap between the environment in the experiment and the expertise in the daily working life of the non-students. But non-students performed worse when they imported irrelevant heuristics into the experiment. Subject pool differences have been rarely analyzed in the realm of deception. One important exception is [25]. They compare students and nuns in a lying experiment and find differences between the subject pools (most notably, nuns are lying to their disadvantage in individual decision problems) [26]. Points out that the experiences of non-students are only helpful if the expertise of the professionals is relevant to the task in the lab and that the professionals also recognize that expertise is relevant.

To shed further light on possible differences between subject pools, we recruit both students and non-students. The non-students are chess players who are not enrolled in a degree program at a university. Chess players seem to be interesting for our experiment because they have training in strategic interactions. While playing chess, individuals not only have to think about objectively good moves but also form expectations about how the opponent might react to them. For example, an objectively perfect move could work out poorly in practice if it leads to variations where the opponent is an expert in. Similar to our experiment, in chess usually two people play against each other. Moreover, by reminding them that we are looking for chess players, there might be some weak form of priming ([27]). As [28] have pointed out people have different identities. The subjects may be in a competitive mood when they are reminded of their identity as a chess player (in chess there are only 3 outcomes: draw, win or lose).

The rest of the paper is organized as follows: Section 2 provides the experimental design. Section 3 describes the behavioral research questions. After presenting the approach to data analysis (Section 4), we describe the experimental subjects (Section 5) and analyze the data (Section 6). Section 7 concludes.

2. Experimental design

2.1. Basic design

The basic structure of the experiment is adopted from [17]’s (2005) 2-person deception game. The identity of the players is anonymized (for both players). It is common knowledge that player 1 has private information. The two players play against each other in a one-shot experiment. There are several reasons to carry out the experiment as a one-shot game [29]. Point out that many games are played uniquely in reality [30]. Remarks that people face many important decisions for a limited number in life (e.g. choosing a degree program, a spouse, or whether or not to buy a house). Furthermore, many entrepreneurial decisions are made irregularly in the sense that the economic framework conditions are bound to change at all times (e.g. capital restructuring, mergers). According to [31], issues such as reputation formation and signaling can be avoided through one-shot games. It also rules out learning effects and strategic behaviors (e.g. reciprocity).

Player 1 (Sender of the message)

Player 1 is fully informed about the payoffs for herself and her opponent (i.e., for both options A and B; see Table 1). Player 1 sends a message to player 2, indicating which option (A or B) results in a higher payoff for player 2. This message can be true or false. The message itself does not affect the payoffs of the players. In other words, it is cheap talk. The experiment consists of two decision situations. For both of them applies: Player 1 lies if she claims that option B leads to a higher payoff for player 2 than option A. Player 1 maximizes her payoffs if option B in situation 1 and option A in situation 2 were actually played. Note that for situation 1 this would be in line with a lie and for situation 2 it would be consistent with an honest message. To keep it simple, we stick to the terminology of [17] in this paper. However, we would like to point out that this dichotomy (honest vs. deception) could also be seen critically. For example, as [32] correctly points out honest messages could also be classified as deception if one has the expectation that the receiver does not follow the message.

Table 1

Payoffs for the players in both situations (from the perspective of player 1) (a).

Situation 1: Altruistic renunciation (b)			Situation 2: Costly punishment (b)
Option	Player 1	Player 2	Option	Player 1	Player 2
A	9	12	A	6	15
B	10	3	B	5	5

(a) We presented situation 1 to the subjects first. We cannot exclude the possibility of order effects, which has to be analyzed in follow-up studies.

(b) We did not communicate the labels assigned to the situations to the experimental subjects. In contrast, we used the neutral framings “situation 1” and “situation 2.”

Player 2 (Receiver of the message)

Player 2 has no information about the payoffs. She only knows the (possible) messages of player 1. However, player 2 picks one of the two options A or B, which is payoff-relevant for both players (common knowledge to both players).

2.2. Treatments

We extend [17] by considering systematic variations of the initial endowment. Altogether, we examine 3 scenarios (1 reference scenario and 2 treatment scenarios; Table 2). The experimental subjects were randomly assigned to one scenario only. To increase the statistical power of our analysis, subjects had to respond to both situations within one endowment scenario (between-subjects study design). We refrain from using a within-subjects study design (each experimental subject makes decisions in all endowment scenarios), as the subjects may activate different emotions in the treatments. Player 1 and player 2 know that the initial endowment in the respective treatments and are aware that it is common knowledge to both players.

Table 2

Treatment conditions (endowment scenarios).

	Player 1	Player 2
Benchmark (reference scenario)	€0	€0
Treatment I	€10	€0
Treatment II	€0	€10

Short summary of the experimental design. Player 1 is entirely informed about the payoffs associated with the two options of action and has private knowledge about the payoffs. Player 1 sends player 2 a message (either true or wrong; cheap talk) about her alleged payoffs. Player 2 only knows the possible messages from player 1 and the endowment of both players. However, the choice made by player 2 determines the payoffs of both players.

2.3. Subjects, incentives, and language

2.3.1. Subjects

We recruit both university students as well as non-students (the latter are also members of a chess club). Students are recruited via the online learning platform “StudIP” of the Martin Luther University Halle-Wittenberg, where the link to the experiment was placed. The prerequisite to joining the experiment was that individuals were enrolled as students in a degree program at a university. The recruitment of the non-student chess players was carried out as follows: we contacted several chess clubs in Germany as well as people with the request to attend /advertise the study. For example, the German master (GM Niclas Huschenbeth) shared the link to the study on his social media platform. The support of ChessBase GmbH (a German company that produces chess software and operates the Internet chess server “playchess.com”) was very helpful to recruit the target number of subjects. A total of 30 individuals are recruited per treatment and population (i.e., a total of 180 of each population). The number of participants was primarily determined by the research budget.

2.3.2 Incentives

To increase the overall willingness to attend the experiment, ten subjects are randomly selected and awarded a show-up fee of €50. Moreover, we provided monetary incentives which were linked to decisions and a chance mechanism. A total of 20% of the subjects in the role of player 1 as well in the role of player 2 are randomly selected and paired with another subject from the same population. Subjects in the role of player 1 had to decide in two situations. We flipped a coin (i.e., p = 0.5) to determine which of the two decision situations were to be paid (i.e., random lottery payment technique). All amounts of money shown in the experiment correspond to the real €-values.

2.3.4 Language

We use neutral language (i.e., loaded terms, such as “deception” are not used).

3. Behavioral research questions

Research questions depend on the underlying concept of man. A rational profit maximizer is often used as a benchmark for actual human behavior. However, we would like to discuss the research questions primarily on the basis of a more comprehensive model of man. We assume that individuals do not only want to achieve high payoffs but also have non-negligible preferences about the distribution of wealth/endowment. Following [8], we assume that there are three determinants that are (potentially) relevant for the utility function of an individual. For illustration purposes, this will be presented formally (although the formula will not be used later in the paper): Ui(x) = xi− αi max {xj−xi,0}– βi max {xi−xj,0}, i ≠j, where the first term denotes the monetary payoff of player i, the second term describes monetary disadvantageous inequality, and the third term denotes monetary advantageous inequality. In other words, individuals dislike inequality. From a psychological point of view, it seems plausible to assume α > β, i.e. that inequality is perceived more unpleasantly if one is in a monetarily disadvantageous situation.

In our research questions, we distinguish between sender behavior (i.e., the sender of the message, player 1) and receiver behavior (i.e., the receiver of the message, player 2).

3.1. Sender behavior

3.1.1. To what extent does player 1 resort to honest behaviors in the reference scenarios?

A rational profit maximizer favors B in situation 1 and A in situation 2 (if the opponent is assumed to follow one’s message). Both options generate a monetary surplus of €1 for player 1 in the entire experiment. However, experimental studies of similar contexts indicate that individuals are willing to forego money-maximizing alternatives (for example when there are violations of social norms [33, 34]). Humans have multiple goals ([35]). These include an aversion to inequality or allocations that are perceived as unfair. The honest player 1 proposes in situation 1 an option of action which costs €1 for himself but increases the outcome for player 2 by €9 (altruistic renunciation). Honesty in situation 2 is associated with a message that would lead to a higher monetary outcome for both players. However, the benefit for player 1 amounts to only €1 while the other player receives a plus of €10. Player 1 may find this unjustified and decides to forego the €1 by choosing the egalitarian action option B (costly punishment). Since the decision of player 2 is payoff-relevant, the expectations of player 1 about whether player 2 follows the message or not plays a role. In his experimental study [17], found that slightly more than 80% of the subjects in the role of player 1 have had the expectation that the other player follows the message.

3.1.2 How does the variation of the initial endowment affect honest messaging?

Systematic variation of the endowment creates inequality. Following [8], we assume that inequality is perceived as unpleasant to some extent. This may influence expectations about the opponent’s behavior.

In treatment 1, player 1 has an initial endowment of €10; player 2 has €0. This surplus may lead to some psychological costs for player 1 due to inequality aversion or fairness preferences. As a result, player 1 is probably more willing to opt for pro-social options (compared to the reference scenario). In addition, player 1 may expect that player 2 trusts player 1 more (in a slightly more formal expression: player 1 expects that player 2 thinks that player 1 is willing to share a small fraction of the larger cake and therefore player 2 tends to follow the message of player 1). Thus, we assume that player 1 behaves more honestly than in the benchmark scenario. In other words: in situation 1, player 1 is more inclined to give up a small amount in order to prevent player 2 from being significantly worse off; in situation 2, player 1 is less inclined to propose option B (i.e., the egalitarian outcome), which is significantly monetarily detrimental to player 2.

In treatment 2, player 1 has an initial endowment of €0; player 2 has €10. This gap is probably perceived by player 1 as unpleasant (e.g. unjust or unfair). Player 1 might compensate this with a (compared to the benchmark scenario) reduced willingness to welcome a relatively high payoff for player 2. In other words, player 1 is more willing to lie (i.e., declare option B advantageous in both decision situations).

3.1.3 Do non-students act as if they were more honest than students?

Various studies find that non-students tend to be more pro-social than students ([20, 22, 31, 36, 37]). Greater pro-sociality towards the opponent means that player 1 increasingly falls back on honest alternatives of action: In situation 1, player 1 renounces €1 so that the opponent does not perform significantly worse; in situation 2, player 1 accepts inequality in which the opponent performs significantly better (instead of sacrificing €1 for equality).

3.1.4 What other determinants can explain the decision-making behavior of player 1?

The first 3 research questions dealt with the variables of expectation of the behavior of the opponent, treatment 2, treatment 3, and the population of interest (students vs. non-students). Now a bunch of other associations between the propensity to be honest and the following variables will be exploratory examined: victim sensitivity, beneficiary sensitivity, religiosity, interpersonal trust, gender, political view, age, and net income.

The perception of injustice and the reaction to injustice differs between people ([38]). We investigate the individual perceived disutility when others are undeservingly better off than one-self (victim sensitivity) and when oneself is better off for no reason (beneficiary sensitivity). The effect of religiosity cannot be determined unequivocally ex-ante. For example [39], present theoretical arguments for both positive and negative effects. Religiosity can promote that one is more cooperative towards other people (i.e., doing something good for others) as well as being intolerant towards people with a different background. Interpersonal trust matters for the performance of institutions. For example [40], describe a negative relationship between trust and transaction costs. Experiences with other people may play a role in whether one is more pessimistic or optimistic about other people. Various studies describe differences in gender: [41] find that women are more egalitarian than men [42]; summarize in their literature review that women tend to be on average more risk-averse than men. With regard to the relevance of political views [41], “surprisingly” find no noteworthy differences between people who prefer right-wing parties and people who favor left-wing parties in terms of equality. Beyond that, humans are subject to change with age. This includes changes in the brain with age ([43]). Furthermore, life experiences increase with age. In addition, we examine the role of net income: the higher the income the less costly might generous behavior be.

3.2 Receiver behavior

3.2.1 To what extent does player 2 trust the message from player 1 in the reference scenario?

Player 2 only knows the (potential) messages of player 1 in the benchmark scenario. This is cheap talk and should not play a role according to rational choice theory. Nevertheless [17], found that almost 80% of those who acted in the role of player 2 followed payer 1’s message. Therefore, it can be assumed that a large proportion of the subjects follows the message of player 1.

In treatment 1, player 2 has an initial endowment of €0; player 1 has €10. Player 2 expects player 1 to be ready to give away some of the cake. In other words, player 2 expects player 1 to tend to act more honestly. Therefore, compared to the reference scenario, player 2 is more likely to follow the message of player 1.

In treatment 2, player 2 has an initial endowment of €10; player 1 has €0. Player 2 expects that player 1 considers the situation to be unfair and fears adverse discrimination. Therefore, player 2 is more probable (compared to the reference scenario) not to follow player 1’s message (compared to the reference scenario).

3.2.3 Do non-students rather than students tend to trust Player 1’s message?

A higher level of pro-sociality among the non-students can result in player 2 trusting the opponent more. Furthermore, it is conceivable that non-students are more willing to tolerate monetary disadvantageous inequality. Therefore, we assume that non-students follow the messages systematically more often than students do.

3.2.4 What other determinants can explain the decision-making behavior of player 2?

A bunch of associations between the propensity to trust player 1 and the following variables will be examined exploratory: victim sensitivity, beneficiary sensitivity, religiosity, interpersonal trust, gender, political view, age, education, and net income (for a description of the variables, see the Sender behavior section above, research question 4).

3.3. Outcome of bargaining

The highest outcome in terms of financial assets, defined as the sum of the individual payoffs of player 1 and player 2, can be realized when player 2 selects option A. Which scenario is most in line with Bentham’s utilitarian greatest happiness principle? We expect player 1 to increasingly opt for option A in treatment 1 (compared to the baseline scenario) and player 2 to be inclined to follow this message. Compared to the benchmark scenario, presumably fewer subjects in the role of player 1 opt for option A in Treatment 2, but also fewer subjects trust the message. The overall effect is unclear and an empirical/experimental question. However, we suspect that the sender’s renunciation of option A is greater than the decline in the receiver’s trust. In other words, the bargaining outcome would be greater for treatment 1 than for treatment 2 (Table 3).

Table 3

Expected bargaining outcome.

Treatment	Sender behavior	Receiver behavior	∑(Player 1 + Player 2)
1 (player 1 + €10)	Option A↑	Trust↑	T1 > T2
2 (player 2 + €10)	Option A↓	Trust↓

4. Approach to data analysis

The institutional review board approval has been obtained by the German Association for Experimental Economic Research e.V. (No. sZXeRf5E). The design and approach to data analysis has been pre-registered (AER RCT Registry; AEARCTR-0005399).

4.1 Regression analysis

We deal with two primary outcome variables that depend on the role the experimental subjects have been assigned to. We are interested in whether the subjects send an honest or dishonest message if they play in the role of player 1 (“Decision player 1”) and, if they are assigned to the role of player 2, whether they follow or not follow the message. It is important to consider subjects’ expectations about the likely behavior of others because both preferences and beliefs matter (which is similar to public goods experiments, for example). A summary of the variables we take into consideration and a brief explanation is given in Table 4. If two or more items/questions are combined (e.g. beneficiary sensitivity) the calculation follows the procedure where the items/questions have been taken from. In the following, we take a look at our main specifications of the regression analysis. The questions/statements and their respective values are depicted in Table 4.

Table 4

Summary of variables and their measurement.

Variable	Question / Statement	Values
Student	Are you enrolled as a student at a university?	Yes = 1, No = 0 (i.e., “Non-student” reverse)
Degree program (if Student = 1)	In which degree program are you enrolled?	List of several degree programs + option to add another one
Federal state	In which federal state do you live (main residence)?	Saxony-Anhalt (1), Saxony (2), Thuringia (3), Mecklenburg Western Pomerania (4), Brandenburg (5), Berlin (6), Bavaria (7), Bremen (8), Hesse (9), Hamburg (10), Baden-Württemberg (11), Lower Saxony (12), Northrhine-Westphalia (13), Rhineland Palatinate (14), Saarland (15), Schleswig Holstein (16)
Chess	Do you actively play chess in a club?	Yes = 1, No = 0
Chess activity (if Chess = 1)	How many years have you been playing chess in a club?	#years
Expectation Opponent follows Version: Player 1 (sender)	How many people out of 100 do you think follow your message?	[0;100]
Expectation Opponent follows Version: Player 2 (receiver)	How many people out of 100 do you think have sent you an honest message?	[0;100]
Decision player 1 (sender) [Situation 1 and 2, respectively]	Which message do you want to send to the other player? Option A or Option B?	Message 1 (i.e., honest one) = 1; message 2 (i.e. dishonest one) = 0
Decision player 2 (receiver)	How do you decide yourself? Do you follow the other player’s message or do you decide differently?	1 = Yes, I follow the message; 0 = No, I do not follow the message.
Political view1	In politics people often talk about “left” and “right” to distinguish different attitudes. If yo 33u think about your own political views: Where would you place them? Please answer using the following scale. 0 means”entirely left”, 10 means”entirely right”. You can weigh your answers using the steps between 0 and 10.	[0 entirely left;10 entirely right]
Gender (Female = 1)	What is your gender?	0 = Male, 1 = Female, 2 = Other
Education	Now it’s about your years of education. Please add up the years of school education, training, and university education (if applicable). How many years do you have?	#years
Age	How old are you?	#years
Interpersonal trust2	1) I am convinced that most people have good intentions.2) You can’t rely on anyone these days.3) In general, people can be trusted.	[“don’t agree at all”(1); “agree completely”(5)]
Religiosity1	Do you belong to a church or religious group?	Yes = 1, No = 0
Victim sensitivity3	1) It makes me angry when others are undeservingly better off than me.2) It worries me when I have to work hard for things that come easily to others.	[“not at all”(1); “exactly”(6)]
Beneficiary sensitivity3	1) I feel guilty when I am better off than others for no reason.2) It bothers me when things come easily to me that others have to work hard for.	[„not at all”(1);”exactly”(6)]
Net income	Is your net income	less than €750 (= 1), €750 up to less than €1,500 (= 2), €1,500 up to less than €2,000 (= 3), €2,000 up to less than €2,500 (= 4), €2,500 up to less than €3,000 (= 5), more than €3,000 (= 6)

SOEP-IS Group, 2018. SOEP-IS 2014 –Questionnaire for the SOEP Innovation Sample (Boost Sample, Update soep.is.2016.1). SOEP Survey Papers 518: Series A–Survey Instruments (Erhebungsinstrumente). Berlin: DIW Berlin/SOEP.

Beierlein, C., Kemper, C., Kovaleva, A.J. Rammstedt, B. (2014): Interpersonales Vertrauen (KUSIV3). Zusammenstellung sozialwissenschaftlicher Items und Skalen. doi: 10.6102/zis37 [English version: https://www.gesis.org/fileadmin/_migrated/content_uploads/KUSIV3_en.pdf]

Schmitt, M., Baumert, A., Gollwitzer, M. Maes, J. (2010): The Justice Sensitivity Inventory: Factorial validity, location in the personality facet space, demographic pattern, and normative data. Social Justice Research 23: 211–238. [We use the following short scale: https://zis.gesis.org/skala/Beierlein-Baumert-Schmitt-Kemper-Kovaleva-Rammstedt-Ungerechtigkeitssensibili%C3%A4t-Skalen-8-(USS-8)].

Sender behavior. For each decision situation, we perform a logistic regression because the dependent variable honesty is dichotomous (if yes = 1, otherwise 0). To increase the statistical power, we estimate a fully interactive model (i.e., interactions of the investigated independent variables with the population dummy variable). As coefficients of logistic regressions can only be meaningfully interpreted with respect to signs, we report marginal effects to adequately describe the effect size. We are considering the variables population (non-student, if = 1), expectation opponent version: player 1, and treatments (T1 = treatment 1, T2 = treatment 2). Furthermore, we address psychological and political control variables (political view, interpersonal trust, religiosity, victim sensitivity, beneficiary sensitivity) as well as some other control variables (age, gender, net income). The analysis of the controls is exploratory.

Receiver behavior. The regressions differ from player 1 above only in the dependent variable (trust) and in the independent variable (expectations about player 1 instead of player 2):

Outcome of bargaining. The decision of player 2 determines the payoffs of both players. In both situations, a monetary superior bargaining result could be achieved if option A would have been chosen. Thus, the number of A-outcomes is compared among the three scenarios and both populations. Cramér’s V is used to statistically analyze dichotomous decisions.

4.2 Comment on p-values

There is an intensive debate and discussion on how to use and interpret p-values ([44]). Since this article is not the appropriate place to pursue the discussion in detail, we want to communicate only a few thoughts. While in the past it was quite common to focus on “statistically significant” results, the dichotomy of significant/non-significant is increasingly viewed critically. For example [44], argue “Don’t believe that an association or effect is absent just because it was not statistically significant.” or “In sum, “statistically significant”—don’t say it and don’t use it.”

Notice, in our sample, there are many interaction terms (which deflates p-values) and several variables we looked at (“multiple testing”, which inflates p-values). Therefore, p-values should be cautiously interpreted. The signs and strength of evidence in terms of marginal effects or differences in mean are more meaningful than just looking at p-values.

5. Description of the sample

As pre-registered, the sample comprises 360 subjects (half of which are enrolled in a university degree program and the other half are non-students who are members of a chess club). The size of the sample was primarily driven by budget constraints. It should be noted that there are 11 subjects among the students who also play chess in a club. The average membership of chess players in a club amounts to 27.65 years (SD = 15.06). The vast majority of the students indicated to have their main residence in Saxony-Anhalt (77.22%); the second-highest fraction of participants is from Saxony (7.22%) followed by Schleswig Holstein (3.89%). The residence of the non-students is more widespread across the various federal states: The largest fraction is from Saxony (17.78%), followed by Baden-Württemberg, and Northrhine-Westphalia (both 12.78%). As Table 5 indicates, there are considerable differences but also similarities between the two populations. Among the non-student chess players, 90% associated themselves as male. In contrast, the majority of students is female (63.33%). The fraction of the third gender is very low for both populations (<2%). Due to the low number of the third gender, we stick to the women-men-dichotomy. There is a clear gap in age: non-students are on average considerably older (47.3 years) than students (23.4 years). Moreover, the range of age is broader among non-students than for students (18–33 years and 18–79 years, respectively). On average, non-students (M = 3.78) state their political view to be somewhat more “right” than students (M = 3.32). Students seem to trust other people slightly less (M = 3.54) than non-students (M = 3.71). When asked about belonging to a church or religious group, 30% of non-students and 35.5% of students answered yes. Victim sensitivity, as well as beneficiary sensitivity, is more pronounced, on average, for students than for non-students. As expected, the average net income of non-students (M = 4.16) is substantially higher than that of students (1.31). However, the average number of years of education is quite similar between the populations of students (M = 16.45; SD = 2.84) and non-student chess players (M = 17.63; SD = 3.20).

Table 5

Description of the subjects (N = 360).

		Non-students		Students		Difference
		Mean/Fraction	Std. Dev.	Mean/Fraction	Std. Dev.	Mean/Fraction	Std. Dev.
Gender	Male	90.00	-	35.00	-	55.00	-
	Female	9.44	-	63.33	-	-53.89	-
	Other	0.56	-	1.67	-	-1.11	-
Age		47.33	14.59	23.40	3.23	23.93	11.35
Political view		3.78	2.00	3.32	1.70	0.45	0.30
Interpersonal trust		3.71	0.68	3.54	0.73	0.16	-0.04
Religiosity		0.30	-	0.35	-	-0.05	-
Victim sensitivity		2.78	1.08	3.52	1.19	-0.73	-0.10
Beneficiary sensitivity		2.54	1.17	3.27	1.15	-0.73	0.02
Net income		4.16	1.58	1.31	0.53	2.85	1.05

6. Results

6.1 Behavior of the sender

Table 6 summarizes the decision behavior of the subjects in the role of player 1. Being honest is not in line with a rational money maximizer in situation 1; the opposite applies to situation 2. The willingness to send an honest message is above 75% in the baseline scenario. Interestingly, in both situations, the non-students were slightly more honest than the students. However, the difference is small with 3.33 percentage points in situation 1 (V = -0.0405); in situation 2 it is slightly larger with 10 percentage points 2 (V = -0.1292). This observation can be explained by a higher propensity of non-students to expect the opponent to follow the message in the baseline scenario. However, the subjects in our study were less optimistic than the subjects in [17] who found 82% of the subjects to expect player 2 to follow their message. In our study, only 66.4% (72.4%) of the students (non-students) expect player 2 to follow her message. The correlations between decisions (whether or not to send an honest message) and expectations (that the opponent follows the message) are smaller than we had expected a priori. The correlations are very weak and weak in situation 1; in situation 2 there are also moderate correlations (see Appendix, point-biserial correlation coefficient, player 2). Thus, it seems that there are other variables that might have more explanatory power than the expectation. This is addressed in the regression analysis.

Table 6

Decisions and expectations of player 1 (sender).

		Decision		Expectation
		Honest message in situation 1	Honest message in situation 2	Expectation opponent follows
Students	Baseline	76.67	76.67	M = 66.433, SD = 18.576
	T1	93.33	76.67	M = 62.000, SD = 15.761
	T2	66.67	70.00	M = 60.533, SD = 23.748
Non-students	Baseline	80.00	86.67	M = 72.466, SD = 18.830
	T1	66.67	70.00	M = 60.433, SD = 20.730
	T2	76.67	80.00	M = 72.466, SD = 19.609

1) Honest message means that the message “Option A makes you earn more money” was sent.

In treatment 1, player 1 has an initial endowment of €10 (player 2 has €0), which is why we assumed that player 1 is more inclined to send an honest message to her opponent compared to the benchmark scenario. The expected influence is partially evident among the students. They sent considerably more honest messages in situation 1 (V = 0.2334), whereas no differences can be found in situation 2 compared to the baseline scenario (V = 0.0000). Somewhat surprisingly, non-students did less often send honest messages compared to the baseline scenario (situation 1: V = -0.1508; situation 2: V = -0.2023). Taking a look at the expectations indicates that the behavior of the non-students might be associated with a lower belief that the opponent will follow the message. Since player 1 has an initial endowment of €0 (player 2 has €10) in treatment 2, we assumed that player 2 is less likely to send an honest message compared to the benchmark scenario. In line with that we found that compared to the benchmark scenario, fewer subjects have sent an honest message. The effect is small but seems more pronounced among the students (situation 1: V = -0.1110; situation 2: V = -0.0754) than the non-students (situation 1: V = -0.0405; situation 2: V = -0.0894).

In the following, (for robustness purposes) we take a brief look at the logistic regressions to explain the tendency to send an honest message (Table 7A and 7B). The regression results are by and large in line with what we have found so far. Non-students are more inclined to send an honest message (an exception is specification IIb of Table 7A, where age and expectations were controlled.). The tendency to send an honest message is lower among non-students in treatment 1 than among students. In contrast, the decrease in treatment 2 is relatively pronounced among students, whereas little effect can be found among the non-students.

Table 7

a Regressions to explain honest behaviors. b Regressions to explain honest behaviors.

a
Logit (Marginal effects) Y = 1, message honest Y = 0, else	Situation 1
	Ia		IIa		Ib		IIb
	dy/dx (Std. Err.)	P>|z|	dy/dx (Std. Err.)	P>|z|	dy/dx (Std. Err.)	P>|z|	dy/dx (Std. Err.)	P>|z|
Non-student	0.3869 (0.4548)	0.395	0.2577 (0.4721)	0.585	0.1383 (0.6000)	0.818	-0.1038 (0.5972)	0.862
Treatment 1	0.1438 (0.1035)	0.165	0.1340 (0.1037)	0.196	0.1447 (0.0995)	0.146	0.1328 (0.0962)	0.168
Treatment 1 ∙ Non-student	-0.3891 (0.2613)	0.137	-0.3717 (0.2649)	0.160	-0.3695 (0.2682)	0.168	-0.3357 (0.2678)	0.210
Treatment 2	-0.1593 (0.1334)	0.232	-0.1682 (0.1342)	0.210	-0.1562 (0.1306)	0.231	-0.1658 (0.1293)	0.200
Treatment 2 ∙ Non-student	0.0910 (0.0990)	0.358	0.0953 (0.0942)	0.312	0.1018 (0.0863)	0.238	0.1052 (0.0782)	0.179
Expectation			-0.0024 (0.0023)	0.300			-0.0027 (0.0022)	0.219
Expectation ∙ Non-student			0.0023 (0.0029)	0.422			0.0033 (0.0027)	0.232
Age					-0.0213 (0.0159)	0.179	-0.0235 (0.0156)	0.131
Age ∙ Non-student					0.0158 (0.0162)	0.329	0.0181 (0.0159)	0.257
Female	0.1694 (0.0835)	0.043	0.1775 (0.0809)	0.028	0.1223 (0.0885)	0.167	0.1314 (0.0819)	0.109
Female ∙ Non-student	-0.1837 (0.2598)	0.480	-0.2038 (0.2647)	0.441	-0.1697 (0.2644)	0.521	-0.1963 (0.2706)	0.468
Political view	-0.0493 (0.0290)	0.090	-0.0550 (0.0290)	0.059	-0.0551 (0.0283)	0.052	-0.0633 (0.0283)	0.025
Political view ∙ Non-student	0.0503 (0.0346)	0.146	0.0562 (0.0345)	0.104	0.0498 (0.0340)	0.143	0.0574 (0.0336)	0.088
Religiosity	0.1762 (0.0893)	0.048	0.1796 (0.0874)	0.040	0.1853 (0.0851)	0.029	0.1946 (0.0820)	0.018
Religiosity ∙ Non-student	-0.1953 (0.2168)	0.368	-0.2069 (0.2202)	0.347	-0.2781 (0.2380)	0.243	-0.3122 (0.2471)	0.207
Net income	0.1695 (0.1022)	0.097	0.2031 (0.1129)	0.072	0.2162 (0.1045)	0.039	0.2652 (0.1165)	0.023
Net income ∙ Non-student	-0.1734 (0.1048)	0.098	-0.2071 (0.1151)	0.072	-0.2039 (0.1076)	0.058	-0.2516 (0.1197)	0.036
Trust	0.0195 (0.0660)	0.767	0.0256 (.0667)	0.701	0.0055 (0.0640)	0.931	0.0072 (0.0630)	0.909
Trust ∙ Non-student	-0.0283 (0.0887)	0.750	-0.0338 (0.0888)	0.703	-0.0264 (0.0855)	0.757	-0.0296 (0.0837)	0.723
Victim sensitivity	0.1038 (0.0430)	0.016	0.0940 (0.0439)	0.032	0.0964 (0.0409)	0.018	0.0845 (0.0408)	0.038
Victim sensitivity ∙ Non-student	-0.1006 (0.0553)	0.069	-0.0907 (0.0555)	0.102	-0.1085 (0.0536)	0.043	-0.0971 (0.0526)	0.065
Beneficiary sensitivity	-0.0393 (0.0403)	0.330	-0.0343 (0.0406)	0.398	-0.0291 (0.0391)	0.457	-0.0223 (0.0384)	0.561
Beneficiary sensitivity ∙ Non-student	0.1069 (0.0566)	0.059	0.1005 (0.0566)	0.076	0.0994 (0.0554)	0.073	0.0901 (0.0545)	0.099
Prob > chi2	0.0247		0.0362		0.0122		0.0161
Pseudo R2	0.1712		0.1770		0.1988		0.2072
b
Logit (Marginal effects) Y = 1, message honest Y = 0, else	Situation 2
	Ia		IIa		Ib		IIb
	dy/dx (Std. Err.)	P>|z|	dy/dx (Std. Err.)	P>|z|	dy/dx (Std. Err.)	P>|z|	dy/dx (Std. Err.)	P>|z|
Non-student	0.2650 (0.5199)	0.610	0.3611 (0.5379)	0.502	0.9481 (0.1186)	0.000	0.9499 (0.1167)	0.000
Treatment 1	0.0260 (0.1058)	0.805	0.0348 (0.1031)	0.735	0.0524 (0.1019)	0.607	0.0546 (0.1001)	0.586
Treatment 1 ∙ Non-student	-0.2849 (0.2229)	0.201	-0.2486 (0.2247)	0.269	-0.2942 (0.2263)	0.194	-0.2302 (0.2262)	0.309
Treatment 2	-0.0787 (0.1261)	0.532	-0.0777 (0.1253)	0.535	-0.0667 (0.1232)	0.588	-0.0636 (0.1231)	0.605
Treatment 2 ∙ Non-student	-0.0310 (0.1834)	0.866	-0.0207 (0.1768)	0.906	-0.0203 (0.1764)	0.908	-0.0057 (0.1689)	0.973
Expectation			0.0040 (0.0024)	0.093			0.0035 (0.0023)	0.130
Expectation ∙ Non-student			-0.0017 (0.0032)	0.584			-0.0006 (0.0032)	0.836
Age					0.0341 (0.0202)	0.091	0.0315 (0.0203)	0.122
Age ∙ Non-student					-0.0386 (0.0204)	0.059	-0.0370 (0.0206)	0.073
Female	-0.1714 (0.1222)	0.161	-0.1999 (0.1271)	0.116	-0.0774 (0.1239)	0.532	-0.1066 (0.1300)	0.412
Female ∙ Non-student	0.1301 (0.0918)	0.157	0.1354 (0.0837)	0.106	0.0503 (0.1558)	0.747	0.0549 (0.1524)	0.719
Political view	-0.0139 (0.0286)	0.627	-0.0026 (0.0291)	0.928	0.0019 (0.0300)	0.948	0.0086 (0.0297)	0.772
Political view ∙ Non-student	0.0507 (0.0380)	0.182	0.0353 (0.0384)	0.357	0.0290 (0.0392)	0.460	0.0166 (0.0391)	0.671
Religiosity	-0.1772 (0.1121)	0.114	-0.2034 (0.1191)	0.088	-0.2051 (0.1168)	0.079	-0.2201 (0.1212)	0.069
Religiosity ∙ Non-student	0.1570 (0.0824)	0.057	0.1737 (0.0752)	0.021	0.1475 (0.0857)	0.085	0.1553 (0.0819)	0.058
Net income	-0.0881 (0.0805)	0.274	-0.0914 (0.0804)	0.256	-0.1518 (0.0895)	0.090	-0.1441 (0.0887)	0.105
Net income ∙ Non-student	0.0702 (0.0860)	0.415	0.0779 (0.0857)	0.363	0.1478 (0.0952)	0.120	0.1492 (0.0944)	0.114
Trust	0.1258 (0.0697)	0.071	0.1028 (0.0692)	0.138	0.1463 (0.0721)	0.043	0.1164 (0.0719)	0.105
Trust ∙ Non-student	-0.1676 (0.1073)	0.118	-0.1545 (0.1066)	0.147	-0.1950 (0.1071)	0.069	-0.1802 (0.1070)	0.092
Victim sensitivity	-0.0570 (0.0421)	0.176	-0.0502 (0.0422)	0.234	-0.0548 (0.0420)	0.192	-0.0500 (0.0423)	0.238
Victim sensitivity ∙ Non-student	0.0993 (0.0647)	0.125	0.0891 (0.0645)	0.167	0.0866 (0.0650)	0.183	0.0765 (0.0653)	0.241
Beneficiary sensitivity	0.0672 (0.0422)	0.112	0.0737 (0.0427)	0.085	0.0663 (0.0418)	0.113	0.0738 (0.0430)	0.086
Beneficiary sensitivity ∙ Non-student	-0.0849 (0.0633)	0.180	-0.0914 (0.0634)	0.149	-0.0829 (0.0625)	0.184	-0.0910 (0.0637)	0.153
Prob > chi2	0.3161		0.2326		0.2080		0.1481
Pseudo R2	0.1099		0.1303		0.1335		0.1545

6.2 Behavior of the receiver

Similar to [17], we find that the majority of subjects in the role of player 2 follow player 1’s message (Table 8). However, in the baseline scenario, there is a gap between students and non-students: whilst only 66.67% of the non-students follow the message of player 1, 80.00% of the students do so (cf., Table 9). This association is small according to Cramer’s V (V = 0.1508). If the opponent has an initial endowment of €10 (i.e., treatment 1), the behavior of both populations deviates only slightly from the baseline scenario. The fraction of students that follow the message from player 1 is a little bit lower than in the baseline scenario (V = -0.0788), whereas the opposite is the case for non-students (V = 0.0358). It should also be mentioned that receivers, who have less initial endowment than their opponents, might not trust the senders because the former could believe that the latter may try to even the payoffs as a fairness criterion. In treatment 2, where player 2 has an initial endowment of €10, both students (V = -0.2182) and non-students (V = -0.1361) follow the message of the opponent much less compared to the respective baseline scenarios. Note that the decision-making behavior of students and non-students in treatment 1 is almost indistinguishable from perfect independence (V = -0.0370). A similar correlation can be found for students and non-students in treatment 2 (V = -0.0673). Since player 2 is only informed about the message sent by her opponent and the initial endowment of both players, it seems plausible that expectations about the likely behavior of the opponent are crucial. The correlations between the decisions (following player 1’s message) and the expectations are middle to strong (see Appendix, point-biserial correlation coefficient, player 2).

Table 8

Decisions and expectations of player 2 (receiver).

		Decision	Expectation
		Follow message of player 1 (= 1)	Expectation opponent sends honest message
Students	Baseline	80.00	M = 63.366, SD = 20.595
	T1	73.33	M = 49.933, SD = 23.648
	T2	60.00	M = 58.533, SD = 18.303
Non-students	Baseline	66.67	M = 56.600, SD = 24.074
	T1	70.00	M = 60.433, SD = 19.890
	T2	53.33	M = 49.800, SD = 24.688

Table 9

Regressions to explain trust behaviors.

Logit (Marginal effects) Y = 1, trust message Y = 0, else	Ia		Ib		Ic		Id
	dy/dx (Std. Err.)	P>|z|	dy/dx (Std. Err.)	P>|z|	dy/dx (Std. Err.)	P>|z|	dy/dx (Std. Err.)	P>|z|
Non-student	-0.1286 (0.2811)	0.647	0.1146 (0.5072)	0.821	0.5801 (0.6007)	0.334	0.7097 (0.5859)	0.226
Treatment 1	0.1242 (0.1226)	0.311	0.1208 (0.1226)	0.325	0.1207 (0.1473)	0.412	0.2793 (0.1178)	0.018
Treatment 1 ∙ Non-student	-0.2239 (0.2436)	0.358	-0.2021 (0.2427)	0.405	-0.1278 (0.2323)	0.582	-0.4110 (0.3107)	0.186
Treatment 2	-0.2268 (0.1497)	0.130	-0.2245 (0.1487)	0.131	-0.1010 (0.1477)	0.494	-0.1090 (0.1492)	0.465
Treatment 2 ∙ Non-student	0.1440 (0.1255)	0.251	0.1443 (0.1227)	0.239	-0.0450 (0.1946)	0.817	0.0853 (0.1365)	0.532
Expectation	0.0153 (0.0031)	0.000	0.0151 (0.0031)	0.000	-		0.0134 (0.0032)	0.000
Expectation ∙ Non-student	0.0009 (0.0050)	0.849	0.0009 0.0050)	0.853	-		0.0042 (0.0057)	0.459
Age			-0.0012 (0.0157)	0.937	0.0016 (0.0160)	0.919	0.0067 (0.0158)	0.672
Age ∙ Non-student			-0.0041 (0.0161)	0.800	-0.0056 (0.0164)	0.732	-0.0114 (0.0163)	0.484
Female					0.0851 (0.1139)	0.455	0.0541 (0.1136)	0.634
Female ∙ Non-student					-0.2561 (0.24146)	0.289	-0.2285 (0.4162)	0.583
Political view					-0.0001 (0.0372)	0.997	-0.0028 (0.0355)	0.937
Political view ∙ Non-student					-0.0248 (0.0453)	0.583	-0.0461 (0.0462)	0.318
Religiosity					0.2055 (0.1066)	0.054	0.1651 (0.0952)	0.083
Religiosity ∙ Non-student					-0.3605 (0.2065)	0.081	-0.2342 (0.2612)	0.370
Net income					-0.1419 (0.1150)	0.217	-0.0430 (0.1075)	0.689
Net income ∙ Non-student					0.1595 (0.1191)	0.180	0.0803 (0.1137)	0.480
Trust					0.2427 (0.0824)	0.003	0.1815 (0.0733)	0.013
Trust ∙ Non-student					-0.1089 (0.1116)	0.329	-0.1187 (0.0997)	0.234
Victim sensitivity					-0.0241 (0.0501)	0.630	-0.0372 (0.0492)	0.449
Victim sensitivity ∙ Non-student					-0.0075 (0.0715)	0.916	-0.0524 (0.0786)	0.505
Beneficiary sensitivity					0.0611 (0.0546)	0.263	0.0516 (0.0468)	0.270
Beneficiary sensitivity ∙ Non-student					-0.0208 (0.0697)	0.765	0.0067 (0.0653)	0.918
Prob > chi2	0.0000		0.0000		0.0233		0.0000
Pseudo R2	0.3438		0.3534		0.1581		0.4436

The regression analysis to explain trust behavior provides some interesting insights (Table 9). Specification 1a shows that the dummy non-student is negatively associated with the tendency to follow the opponent’s message. The comparison of specification 1a and 1b indicates that this effect is reversed when controlling for the variable age (specifications 1b to 1d). Moreover, the regressions show a strong effect for treatment 2. The control religiosity has a substantial, positive effect which is, however, only positive for the students.

6.3 Outcome of bargaining (welfare analysis)

To maximize the sum of the payoffs of both players, it would be best to play option A as often as possible (cf., Section 2). In situation 1, option A (9+12) exceeds option B (10+3) by €8; option A (6+15) exceeds option B (5+5) by €11 in situation 2. The variable of interest is how often option A has been played. Welfare analysis requires the two variables “Honest message” (H) and “Following message” (F). The fraction of expected A-outcomes (i.e., realized honest option) can be calculated by EA = H · F + (1–H) · (1–F). Let us assume, for example, that H = 0.7667 and F = 0.8 is given. Thus, the expected fraction of A outcomes equals 61.336 + 4.666 = 66.002. The expected bargaining outcomes of our experimental study are summarized in Table 10.

Table 10

Expected fraction of A’s (payoff-superior outcome).

		Expected A-realizations in situation 1	Expected A-realizations in situation 2
Students	Baseline	66.002	66.002
	T1	70.217	62.444
	T2	53.334	54.000
Non-students	Baseline	60.002	62.225
	T1	56.668	58.000
	T2	51.776	51.998

The main findings can be summarized as follows:

Treatment 1 (where player 1 has an initial endowment of €10, whereas player 2 has €0) results in a better bargaining outcome than treatment 2 (where player 1 has an initial endowment of €0, whereas player 2 has €10), regardless of the population. The distribution of the initial endowment appears to be non-allocation-neutral.

At the aggregate level, students and non-students earn less money in treatment 2 than in the baseline scenario.

7. Conclusion

The paper addressed the behavioral influence of differences in initial endowment on the tendency to send an honest message and to trust others. It also dealt with the question of whether students and non-students differ in their behaviors. For this purpose, we adopted the basic design of [17]’s (2005) two-player deception game and extended it to two points: differences in the initial endowment and different subject pools (students and non-student chess players). The non-students are, on average, much older, earn more money, and have a systematically different gender distribution. Overall, students can be described as quite homogeneous, and non-student chess players rather heterogeneous with spite to their personal characteristics. Can different behavior patterns be observed in the experiment between the two populations? Reminding the subjects of their identity might be a driver for differences.

We find that non-students more often send honest messages. Students send more honest messages when their initial endowment increases, whereas the opposite holds for non-students. If the initial wealth of the opponent increases, students react by sending muss less honest messages. In contrast, the non-student chess players did not change their behavior in this situation. Interestingly, students are more likely to trust the opponent’s message. Both, the students and non-students, a much less likely to trust others when their own endowment increases. Thus, we can conclude that there is no clear evidence of whether students or non-students behave more pro-socially.

Replication studies must show whether our findings are artifacts or systematical. For example, it is an open question whether order effects influenced our results. In addition, other levels of the initial endowment (we used €10) and the emotions which are associated with such differences should be analyzed. Moreover, further studies are required if the findings are robust if the games are played for multiple rounds. For example [45], model deception as a multi-period bargaining process in which in an early stage a relationship is established with the victim to exploit it in a later stage.

(PDF)

Click here for additional data file.

(DOCX)

Click here for additional data file.

1 Oct 2021

A rebuttal letter that responds to each point raised by the academic editor and reviewer(s). You should upload this letter as a separate file labeled 'Response to Reviewers'.

A marked-up copy of your manuscript that highlights changes made to the original version. You should upload this as a separate file labeled 'Revised Manuscript with Track Changes'.

An unmarked version of your revised paper without tracked changes. You should upload this as a separate file labeled 'Manuscript'.

If you would like to make changes to your financial disclosure, please include your updated statement in your cover letter. Guidelines for resubmitting your figure files are available below the reviewer comments at the end of this letter.

If applicable, we recommend that you deposit your laboratory protocols in protocols.io to enhance the reproducibility of your results. Protocols.io assigns your protocol its own identifier (DOI) so that it can be cited independently in the future. For instructions see: https://journals.plos.org/plosone/s/submission-guidelines#loc-laboratory-protocols. Additionally, PLOS ONE offers an option for publishing peer-reviewed Lab Protocol articles, which describe protocols hosted on protocols.io. Read more information on sharing protocols at https://plos.org/protocols?utm_medium=editorial-email&utm_source=authorletters&utm_campaign=protocols.

We look forward to receiving your revised manuscript.

Kind regards,

Pablo Brañas-Garza, PhD Economics

Academic Editor

PLOS ONE

Journal Requirements:

When submitting your revision, we need you to address these additional requirements.

1. Please ensure that your manuscript meets PLOS ONE's style requirements, including those for file naming. The PLOS ONE style templates can be found at

https://journals.plos.org/plosone/s/file?id=wjVg/PLOSOne_formatting_sample_main_body.pdf and

https://journals.plos.org/plosone/s/file?id=ba62/PLOSOne_formatting_sample_title_authors_affiliations.pdf

2. Please update your submission to use the PLOS LaTeX template. The template and more information on our requirements for LaTeX submissions can be found at http://journals.plos.org/plosone/s/latex

3. We note that you have stated that you will provide repository information for your data at acceptance. Should your manuscript be accepted for publication, we will hold it until you provide the relevant accession numbers or DOIs necessary to access your data. If you wish to make changes to your Data Availability statement, please describe these changes in your cover letter and we will update your Data Availability statement to reflect the information you provide

4.  Please include your full ethics statement in the ‘Methods’ section of your manuscript file. In your statement, please include the full name of the IRB or ethics committee who approved or waived your study, as well as whether or not you obtained informed written or verbal consent. If consent was waived for your study, please include this information in your statement as well

[Note: HTML markup is below. Please do not edit.]

Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Author

1. Is the manuscript technically sound, and do the data support the conclusions?

The manuscript must describe a technically sound piece of scientific research with data that supports the conclusions. Experiments must have been conducted rigorously, with appropriate controls, replication, and sample sizes. The conclusions must be drawn appropriately based on the data presented.

Reviewer #1: Yes

**********

2. Has the statistical analysis been performed appropriately and rigorously?

Reviewer #1: Yes

**********

3. Have the authors made all data underlying the findings in their manuscript fully available?

The PLOS Data policy requires authors to make all data underlying the findings described in their manuscript fully available without restriction, with rare exception (please refer to the Data Availability Statement in the manuscript PDF file). The data should be provided as part of the manuscript or its supporting information, or deposited to a public repository. For example, in addition to summary statistics, the data points behind means, medians and variance measures should be available. If there are restrictions on publicly sharing data—e.g. participant privacy or use of data from a third party—those must be specified.

Reviewer #1: Yes

**********

4. Is the manuscript presented in an intelligible fashion and written in standard English?

PLOS ONE does not copyedit accepted manuscripts, so the language in submitted articles must be clear, correct, and unambiguous. Any typographical or grammatical errors should be corrected at revision, so please note any specific errors here.

Reviewer #1: Yes

**********

5. Review Comments to the Author

Please use the space provided to explain your answers to the questions above. You may also include additional comments for the author, including concerns about dual publication, research ethics, or publication ethics. (Please upload your review as an attachment if it exceeds 20,000 characters)

Reviewer #1: Summary

The aim of the paper is to better understand the interplay between inequality and deception. To study it they run an experiment using a sender-receiver game where initial endowment of participants vary. Additionally, they compare students and chess players. They find that chess players are more honest, that students trust the message send by senders more often and that initial endowment affects different populations in different ways.

Overall evaluation

In my opinion the paper is interesting and answers an important question in the literature. In spite of this, I have the feeling that it has some flaws. First, the objective of the paper and its importance in the literature should be clarified. Second the design should be clearer for the reader and finally I would clarify the hypothesis and results. You can see all my comments below.

Main comments

- I think that you can further improve the abstract by simplifying the explanation about the basic game and enhancing your differences with it and what you add to the literature, by for example explaining what type of endowment variations you introduce.

- I would mention that your main interest is to study lying to another subject rather than to yourself and that is why you choose the mentioned task instead of the die experiment (Shalvi et al. 2012; Fischbacher and Follmi Heusi, 2013; Charness et al. 2019) or a real effort task (Mazar et al. 2008; Groulleau et al. 2016).

- There are very few experiments in deception with non-students. One example is Utikal and Fischbacher (2013). They use a different task but find differences between the behavior of students and a very specific population, nuns. This comparison is therefore similar to yours.

- Chess players are used to two people game but they are also a population always playing a game where dishonesty if highly punished and socially non-acceptable. This can also affect their behavior. You need to further justify your choice of non-student population. Do you have any information on income? It may be the case that the payoff is less important for adult chess players than for college students.

- I would explain a little bit better the design in the introduction part so that the reader knows what you mean by a variation of the sender-receiver game.

- I have issues following the design. Do they decide the message for both type of payoffs? Please justify why you chose those endowments. Option A (not cheating) is always more efficient but more in situation 1 than 2 for example. When are different endowments announced and how? Because since there is not an effort task it seems that the initial endowment is due to luck which can affect the entitlement over this amount. I would rename the treatments to something more intuitive so that we do not mix them. For example, Poor/rich sender or something similar.

- If they choose their option for both type of situations it may be the case that you have order effects. Did you control for this?

- I would state hypotheses instead of the current way you present your expected results. It is now a little bit confusing to follow this section. This would also make easier to follow the rest of the sections.

- You have regressions controlling for senders who believe receiver follow their message. Do you obtain the same if you leave out strategic senders?

Other comments

- I think that mentioning the main results in the introduction could add to the paper.

- You probably mean payed instead of played in the sentence below. Otherwise I do not understand the meaning of the sentence.

“Subjects in the role of player 1 had to decide in two situations. We flipped a coin (i.e., p = 0.5) to determine which of the two decision situations were to be played (i.e., random lottery payment technique)”

- I would not introduce the formula of Fehr and Schmidt (1999) if I am not using it again in the rest of the paper. It can be misleading.

- I do not see the point of having part 4.2.

- You need to further explain why you ask senders about their expectation regarding what receivers will do (Sutter, 2009). As it is now I am not aware that you controlled for this until the results section.

- It may be the case that when receivers have a low endowment they do not trust senders because they may believe that they will try to even the payoffs.

- You find some gender differences in behavior. There are multiple papers in gender differences in dishonesty finding different results (Dreber and Johannesson, 2008; Gylfason et al., 2013; Ezquerra et al. 2018). It could add to the paper to mention and discuss what you find related to gender.

References

Charness, G., Blanco-Jimenez, C., Ezquerra, L., & Rodriguez-Lara, I. (2019). Cheating, incentives, and money manipulation. Experimental Economics, 22(1), 155-177.

Gylfason, H. F., Arnardottir, A. A., & Kristinsson, K. (2013). More on gender differences in lying. Economics Letters, 119(1), 94-96.

Dreber, A., & Johannesson, M. (2008). Gender differences in deception. Economics Letters, 99(1), 197-199.

Ezquerra, L., Kolev, G. I., & Rodriguez-Lara, I. (2018). Gender differences in cheating: Loss vs. gain framing. Economics Letters, 163, 46-49.

Fischbacher, U., & Föllmi-Heusi, F. (2013). Lies in disguise—an experimental study on cheating. Journal of the European Economic Association, 11(3), 525-547.

Grolleau, G., Kocher, M. G., & Sutan, A. (2016). Cheating and loss aversion: Do people cheat more to avoid a loss?. Management Science, 62(12), 3428-3438.

Mazar, N., Amir, O., & Ariely, D. (2008). The dishonesty of honest people: A theory of self-concept maintenance. Journal of marketing research, 45(6), 633-644.

Shalvi, S., Eldar, O., & Bereby-Meyer, Y. (2012). Honesty requires time (and lack of justifications). Psychological science, 23(10), 1264-1270.

Utikal, V., & Fischbacher, U. (2013). Disadvantageous lies in individual decisions. Journal of Economic Behavior & Organization, 85, 108-111.

**********

6. PLOS authors have the option to publish the peer review history of their article (what does this mean?). If published, this will include your full peer review and any attached files.

If you choose “no”, your identity will remain anonymous but your review may still be made public.

Do you want your identity to be public for this peer review? For information about this choice, including consent withdrawal, please see our Privacy Policy.

Reviewer #1: No

[NOTE: If reviewer comments were submitted as an attachment file, they will be attached to this email and accessible via the submission site. Please log into your account, locate the manuscript record, and check for the action link "View Attachments". If this link does not appear, there are no attachment files.]

While revising your submission, please upload your figure files to the Preflight Analysis and Conversion Engine (PACE) digital diagnostic tool, https://pacev2.apexcovantage.com/. PACE helps ensure that figures meet PLOS requirements. To use PACE, you must first register as a user. Registration is free. Then, login and navigate to the UPLOAD tab, where you will find detailed instructions on how to use the tool. If you encounter any issues or have any questions when using PACE, please email PLOS at figures@plos.org. Please note that Supporting Information files do not need this step.

Submitted filename: Referee report PONE.pdf

Click here for additional data file.

8 Nov 2021

PONE-D-21-22531

Is there a link between endowment inequality and deception? – An analysis of students and chess players

Reply to the reviewers

We very much appreciate the reviewers’ thorough reading of our manuscript as well as their very thoughtful comments. In the following, we have listed the reviewers’ comments along with our replies and the cross reference to the changes implemented in the manuscript.

1 Reviewer 1

- I think that you can further improve the abstract by simplifying the explanation about the basic game and enhancing your differences with it and what you add to the literature, by for example explaining what type of endowment variations you introduce.

The basic design is described as follows:

“This paper investigates experimentally the relationship between inequality in endowment and deception. Our basic design is adopted from Gneezy (2005): two players interact in a deception game. It is common knowledge that player 1 has private information about the payoffs for both players of two alternative actions. Player 1 sends a message to player 2, indicating which alternative putatively will end up in a higher payoff for player 2. The message, which can either be true or false, does not affect the payoffs of the players. Player 2 has no information about the payoffs. However, player 2 selects one of the two alternatives A or B, which is payoff-relevant for both players.”

The added value to the literature is explained:

“Our paper adds value to the literature by extending Gneezy (2005) in two elements. First, we systematically vary the initial endowment of the players 1 and 2 (common knowledge to both of them). Second, we do not limit ourselves to the standard population of university students but also recruit chess players that are not enrolled in any degree program. Doing so, we want to find out if our results remain robust over a non-standard subject population which is known to be experienced to some extent in strategic interactions.”

We would like to refrain from providing details about the level of the initial endowment because this is not that important to understand the paper itself.

The findings are described as follows:

“Our main findings are: (i) non-students behave more honestly than students, (ii) students are more likely to trust the opponent’s message, and (iii) students and non-students behave differently to variation in initial endowment.”

- I would mention that your main interest is to study lying to another subject rather than to yourself and that is why you choose the mentioned task instead of the die experiment (Shalvi et al. 2012; Fischbacher and Follmi Heusi, 2013; Charness et al. 2019) or a real effort task (Mazar et al. 2008; Groulleau et al. 2016).

We added your point to the paper and now say:

“To study lying to other people (instead of lying to yourself in which the die experiment or a real effort task are quite common; e.g. Grolleau et al. 2016; Charness et al. 2019), our paper adopts the basic design of Gneezy’s (2005) two-player cheap talk sender-receiver game.”

Please notice that we would like to pick the two most recent references. More importantly, we refrain from the Mazar reference because Ariely was involved. We have some serious doubts about this reference. Recently, there was some public attention to a paper of Ariely and doubts about data generation and analysis. For example, a brief discussion about this can be found here: https://datacolada.org/98. It is too risky for us to include Ariely here because we cannot fully replicate the study to find out if it is based on valid research.

- There are very few experiments in deception with non-students. One example is Utikal and Fischbacher (2013). They use a different task but find differences between the behavior of students and a very specific population, nuns. This comparison is therefore similar to yours.

We added the Utikal and Fischbacher (2013) as one of the few experiments with systematic subject pool comparisons to our paper. We now say:

“Subject pool differences have been rarely analyzed in the realm of deception. One important exception is Utikal and Fischbacher (2013). They compare students and nuns in a lying experiment and find differ-ences between the subject pools (most notably, nuns are lying to their disadvantage in individual decision problems).”

- Chess players are used to two people game but they are also a population always playing a game where dishonesty if highly punished and socially non-acceptable. This can also affect their behavior. You need to further justify your choice of non-student population. Do you have any information on income? It may be the case that the payoff is less important for adult chess players than for college students.

We are not sure if chess players are playing a game where dishonesty is highly punished. In chess, people do not want to show their real emotions. For example, if they have a worse position, some players pretend to be completely disinterested in the game. So that the opponent thinks that it must be an easy task to win the game.

Our analysis comprises comparing mean values between the different subject pools and, in a further step, regression analysis. In the regression analysis, we use net income as a control variable. So, yes, you are right that the stakes might be a point for differences but we control for that econometrically.

We agree with you that we should stronger motivate the use of chess players. In the revised version we now consider identity economics as theoretical background in association with the “competition spirit” of chess. We added the following sentences:

“Moreover, by reminding them that we are looking for chess players, there might be some weak form of priming (Cohn and Maréchal 2016). As Akerlof and Kranton (2000) have pointed out people have different identities. The subjects may be in a competitive mood when they are reminded of their identity as a chess player (in chess there are only 3 outcomes: draw, win or lose).”

- I would explain a little bit better the design in the introduction part so that the reader knows what you mean by a variation of the sender-receiver game.

We have added a brief note about the variation of the initial endowment. We now say:

“In our extended Gneezy (2005) design, we provide either player 1 or 2 with an initial endowment of €10 in the treatment conditions.”

We would like to keep it in a brief way because the design is explained in detail in the section after the Introduction.

- I have issues following the design. Do they decide the message for both type of payoffs? Please justify why you chose those endowments. Option A (not cheating) is always more efficient but more in situation 1 than 2 for example. When are different endowments announced and how? Because since there is not an effort task it seems that the initial endowment is due to luck which can affect the entitlement over this amount. I would rename the treatments to something more intuitive so that we do not mix them. For example, Poor/rich sender or something similar.

Yes, the subjects decide for both situations. After allocating the subjects to one treatment, they are informed about the initial endowment (and the initial endowment of the opponent). We have attached the experimental instructions to the manuscript for transparency.

“We extend Gneezy (2005) by considering systematic variations of the initial endowment. Altogether, we examine 3 scenarios (1 reference scenario and 2 treatment scenarios; Table 2). The experimental subjects were randomly assigned to one scenario only. To increase the statistical power of our analysis, subjects had to respond to both situations within one endowment scenario (between-subjects study design). We refrain from using a within-subjects study design (each experimental subject makes decisions in all endowment scenarios), as the subjects may activate different emotions in the treatments. Player 1 and player 2 know that the initial endowment in the respective treatments and are aware that it is common knowledge to both players.”

We are not sure about using label such as “rich” or “poor” because it is too extreme (it was only about €10). However, we tried to find some places in the paper to add reminders about the meaning of the treatments. For example, in Table 3 we added the description of the treatments. Another example is the paragraph above of Table 6 where the treatment conditions were also defined again.

The level of the initial endowment: the short answer is that this is an empirical / experimental question if our level was adequate or not. We thought that even small differences in the initial endowment might infer emotions / inequity aversion. This should be addressed in further research. Therefore, we write in the Conclusion section:

“For example, other levels of the initial endowment (we used €10) and the emotions which are associated with such differences should be analyzed.”

- If they choose their option for both type of situations it may be the case that you have order effects. Did you control for this?

In Table 1, we added the following note:

“We presented situation 1 to the subjects first. We cannot exclude the possibility of order effects, which has to be analyzed in follow-up studies.”

- I would state hypotheses instead of the current way you present your expected results. It is now a little bit confusing to follow this section. This would also make easier to follow the rest of the sections.

We can understand your point by we pre-registered research questions and would like to follow the pre-registration as close as possible to avoid confusion of why we deviate from it. The basic idea was that often null hypotheses are formulated (tests against a non-realistic null hypothesis; cf. John List in a paper on the market of publications) – we did not want to follow this practice.

- You have regressions controlling for senders who believe receiver follow their message. Do you obtain the same if you leave out strategic senders?

I think this is an important topic. In Table 7a and 7b, we provide regressions on both versions (with and without expectations of whether the other person follows/beliefs or not). Direct comparisons are possible and briefly explained in the manuscript.

Other comments

- I think that mentioning the main results in the introduction could add to the paper.

We spent a plenty of time thinking of the pros and cons of adding the results to the Introduction. Yes, there are some journals that follow this practice. We would like to stick with the old version because we think that the reader should first better understand the experimental design. The results depend so much on details in experimental economics. Therefore, we think that talking about the findings could be one version but does not add that much value to the paper.

- You probably mean payed instead of played in the sentence below. Otherwise I do not understand the meaning of the sentence.

“Subjects in the role of player 1 had to decide in two situations. We flipped a coin (i.e., p = 0.5) to determine which of the two decision situations were to be played (i.e., random lottery payment technique)”

Yes, this typo is rather is a rather serious one. Thank you for pointing it out and reading it that carefully. The typo has been corrected (we now write “paid”).

- I would not introduce the formula of Fehr and Schmidt (1999) if I am not using it again in the rest of the paper. It can be misleading.

By providing a formula, we intended to illustrate the components that we are interested in. Some people prefer thinking in form of text, others are better in understanding formulas. So both versions might provide something for both.

- I do not see the point of having part 4.2.

Recently, we experienced that many reviewers argued that nothing can be learned from findings p > 0.05. That’s why we say: “Don’t believe that an association or effect is absent just because it was not statistically significant.” We say this because we have many results p>0.05.

- You need to further explain why you ask senders about their expectation regarding what receivers will do (Sutter, 2009). As it is now I am not aware that you controlled for this until the results section.

In Section 4.1, we now say:

“It is important to consider subjects’ expectations about the likely behavior of others because both preferences and beliefs matter (which is similar to public goods experiments, for example).”

Thank you for this point. We think that making this statement definitely improves clarity of the paper.

- It may be the case that when receivers have a low endowment they do not trust senders because they may believe that they will try to even the payoffs.

To be honest, we were really surprised how complicated such a seemingly simple experiment can be. Our guess was that player 2, who does not have information on the payoff, is more likely to follow player 1 if player 2 thinks that the other player wants to level the payoffs (e.g. due to declining inequality). Here, the formula helps to play a little bit with the determinants.

- You find some gender differences in behavior. There are multiple papers in gender differences in dishonesty finding different results (Dreber and Johannesson, 2008; Gylfason et al., 2013; Ezquerra et al. 2018). It could add to the paper to mention and discuss what you find related to gender.

Regarding gender (which was not pre-registered) we have mixed effects. In the first situation, it seems that women are more likely to send honest messages (which is in line with Dreber and Johannesson 2008). However, in the other situation, the sign of women is negative, but the p-values are very high, so we should be cautious about preliminary findings. Thinking in terms of significant/not-significant, as the other paper do, we would say that we “do not find differences” in situation 2, which is in line with Gylfasion et al. 2013 and Ezquerra et al. 2018. But further research is necessary. However, gender was merely a control variable, not our focus of interest.

2 Reviewer 2

From the abstract and the introduction of your article, the reader could easily identify two goals of the article: contribute to the understanding of the relationship between inequalities and deception and improve the external validity of the results in experimental economics. While I think that the experimental design provides us with one step forward to reaching our first goal, I cannot stop asking, "why should we particularly care about the deceptive behavior of chess players? This question was raised by Frechette (2011) in the discussion when he mentions:

"It also raises the question of what is the group of interest? Who are the agents that are supposed to be represented in those models being tested?"

Thus, how does the selection and understanding of the differences in chess players' behavior, in this case, improve the external validity of your results? I believe that you should develop on answering these questions in your introduction and extending your literature review on different samples of experimental subjects and the implications of observing differences in the behavior of these types in experimental games. Good examples to follow are one given by Abbink and Rochenbak (2006), Alevy et al. (2009), where they explain why understanding the behavior of financial advisors in a cascade game is crucial to improve our understanding of cascades.

We agree with you that we should stronger motivate the use of chess players. In the revised version we now consider identity economics (Akerlof / Kranton) as theoretical background in association with the “competition spirit” of chess. We motivate the recruitment of chess players as follows:

“Chess players seem to be interesting for our experiment because they have training in strategic interactions. While playing chess, individuals not only have to think about objectively good moves but also form expectations about how the opponent might react to them. For example, an objectively perfect move could work out poorly in practice if it leads to variations where the opponent is an expert in. Similar to our experiment, in chess usually two people play against each other. Moreover, by reminding them that we are looking for chess players, there might be some weak form of priming (Cohn and Maréchal 2016). As Akerlof and Kranton (2000) have pointed out people have different identities. The subjects may be in a competitive mood when they are reminded of their identity as a chess player (in chess there are only 3 outcomes: draw, win or lose).”

Furthermore, the introduction of two types of subjects increases your hypothesis. Thus, you should provide power estimations that drive your experimental design and the choice of your number of observations per treatment and correct when needed for multiple hypothesis testing. I don't know if I failed to discover this analysis and values, but it is very important to perform these tasks even more when we have multiple populations.

Thanks for this comment. We now provide reasons for our sample size. We say:

“The size of the sample was primarily driven by budget constraints.”

However, ex post sample size calculations are seen very critically by many scientists. One of the authors has written a paper on power calculations. Just to provide one example:

https://blogs.worldbank.org/impactevaluations/why-ex-post-power-using-estimated-effect-sizes-bad-ex-post-mde-not

As a consequence we would like stick with the budget constraint argument (which was the true reason for our sample size).

When there are multiple subject pools and, in turn, multiple interaction terms, researchers often face multicollinearity. Since this does not influence marginal effects and signs (only makes p-values high), it is not that much a problem if our focus is on signs and coefficients. Multiple hypothesis testing is always a topic. We add this point to the comment on p-values (Section 4.2):

“Notice, in our sample, there are many interaction terms (which deflates p-values) and several variables we looked at (“multiple testing”, which inflates p-values). Therefore, p-values should be cautiously interpreted. The signs and strength of evidence in terms of marginal effects or differences in mean are more meaningful than just looking at p-values.”

While reading the article, I found some style and expression habits that I believe a difficult reader understands your work. For example, the article has several instances where the terms such as Player 1 and Player 2 are used to label tables. Then the reader finds that some other sentences are labeled as sender and receiver, which are used, for example, to name sub-sections of the paper leads the reader in a constant loop of mapping between several different terms to understand the text of your article. It would be an improvement in terms of the article's readability if you could reduce the diversity of terms or use them more systematically. N additional concept that appears to be misleading to any readers is your definition of "Market implications," this Is a two-person game with a context that Vernon Smith classifying inside the "personal exchange" (Smith 2009). There is no market because subjects are not exchanging a good or service, and there is no price or fee. I think that to be more traditional with the economist interpretation of the market and 2 by 2 experimental games; your article will benefit

Thank you. We improved the readability of the paper by not jumping between the terms. Moreover, if the terms player 1 or player 2 were used, we attached the label “sender” and “receiver” if there might be some confusion. Most importantly, in the description of the variables of the paper (Table 4), we now say “player 1 (sender”) instead of only “player 1”, for example. The same has been done for player 2. Similar changes have been made in Table 6 and 8, for example, too.

Following your advice, we now refrain from using the term “market”. Thus, there are some relabeling in the sections 3.3 (research questions), 4.1 (approach to data analysis), and 6.3. (data analysis). We now speak of bargaining outcome.

I believe that the revision of related literature should be expanded, and the text should highlight how alternative theoretical frameworks and previous experiments related to your design and results. For example, little is said about how endowment inequalities affect behavior in other experimental games while there is ample evidence of endowment inequalities among others affecting behavior in trust games such as the one given by: Anderson et al. 2006, Ciriolo 2007, Lei & Vesely 2010, Xiao & Bicchieri 2010, Smith 2011, Brülhart & Usunier 2012, Hargreaves-Heap et al. 2013, Calabuig et al. 2016, Rodriguez-Lara 2018, Bejarano et al. 2018, 2021. Similarly, due to the lack of revision of different theoretical foundations of the relationship between inequality and deception, it appears that there is only one theoretical framework to base your hypothesis is only based on Fehr and Schimdt (1999). A set of new theories of deception Ettinger and Jehiel (2010) or even some interpretations of Mazar et al., 2008 could also inform you, the reader, and other researchers of how your hypothesis and results are in place within the larger literature on deception.

In our revision, we consider some studies which address inequality. This helps to better motivate the research topic of our paper. We say:

“The topic of inequality has been tackled in the experimental literature with mixed findings. For example, in the realm of trust games, Bejarano et al. (2021) found evidence for inequality to matter, whereas Rodriguez-Lara (2018) does not find evidence for inequality aversion.”

Thank you for pointing to the Ettinger and Jehiel (2010) reference. We didn’t know this paper. But it is very interesting. Especially, we like the bargaining idea. Therefore, we added the following sentences in the last section of the paper:

“Moreover, further studies are required if the findings are robust if the games are played for multiple rounds. For example, Ettinger and Jehiel (2010) model deception as a multi-period bargaining process in which in an early stage a relationship is established with the victim to exploit it in a later stage.”

However, we would refrain from the Mazar reference because Ariely was involved. We have some serious doubts about this reference. Recently, there was some public attention to a paper of Ariely and doubts about data generation and analysis. For example, a brief discussion about this can be found here: https://datacolada.org/98. It is too risky for us to include Ariely here because we cannot fully replicate the study to find out if it is based on valid research.

Finally, I consider that your statement regarding p-values and econometric analysis is understandable regarding the analysis. And even after carefully reading your footnote 4" where you stated: "we refrain from using asterisks and provide complete p-values instead, we reduce the number of econometric specifications than originally intended and pre-registered due to space restrictions. For a comprehensive overview of the specification, see the Appendix."

I cannot stop thinking that there is some inconsistency in your analytical approach. First, you stated reduced form regression expressions and present proportions and the outcomes of the statistical tests between proportions. Then you present tables with marginal effects of "only" one reduce form regression, the logit.

But you do not talk about the robustness of the effects to different specifications or the need of clustering the errors, and you present the p-values in these tables. Thus this inconsistency claiming that p-values are not the only important factor and then presenting tables with p-values, but abstaining from defining a clear analytical criterion of analysis difficult readers comprehension of your results. Finally, I can not stop thinking that you do not have many significant results in statistical and non-statistical meaning. Worse than not having significant results is not clearly stating the results or lack of them. I think that the readers would appreciate it if you could clarify the criteria for your analysis. Even if you produce the traditional analysis, show the significance of these results and state your position within the body of the text in the results and discussion section in a more ordinated fashion.

We provide the results for all pre-registered specifications in the paper and some supporting material (robustness checks in the form of correlations, in the Appendix). For example, the zero order correlations are important as a robustness check. There might be some mediator effects in the course of the regression analysis. Therefore, it is important to provide both the correlation analysis (in the Appendix) and the regressions in the manuscript. We only speak of the correlation analysis if there are deviations from the regression analysis. Otherwise it is the same content and only serves as a robustness check.

There are also robustness checks in the regression analysis: for example, there are specifications where the variable expectations has been included and, in another regression, was included. This helps to find out whether the results are “stable.”

We have rewritten the statement on p-values in Section 4.2 and now stronger say, where the focus of the analysis is:

“There is an intensive debate and discussion on how to use and interpret p-values (Wasserstein et al. 2019). Since this article is not the appropriate place to pursue the discussion in detail, we want to communicate only a few thoughts. While in the past it was quite common to focus on “statistically significant” results, the dichotomy of significant/non-significant is increasingly viewed critically. For example, Wasserstein et al. (2019: 1, 2): argue “Don’t believe that an association or effect is absent just because it was not statistically significant.” or “In sum, “statistically significant”—don’t say it and don’t use it.

Notice, in our sample, there are many interaction terms (which deflates p-values) and several variables we looked at (“multiple testing”, which inflates p-values). Therefore, p-values should be cautiously interpreted. The signs and strength of evidence in terms of marginal effects or differences in mean are more meaningful than just looking at p-values.”

We do not only provide logit-regressions: there are mean-values, correlations of the regression analysis as well as robustness checks (zero-order correlations, in the Appendix)

Submitted filename: Revision Chess.docx

Click here for additional data file.

26 Nov 2021

26 Nov 2021

PONE-D-21-22531R1

Is there a link between endowment inequality and deception? – An analysis of students and chess players

PLOS ONE

Many thanks for your comments. Please find attached our response along with the changes we have made in the manuscript.

- You need to further develop the possibility of having different identities. It should be added to the conclusions as a potential explanation for different results. Regarding income how it was calculated should be explained.

�  Thanks for this point. We added the possible reason (different identities) to the Conclusion Section: “Reminding the subjects of their identity might be a driver for differences.”

�  The variables are explained in Table 4. For example, we used several categories to collect data on net income: “less than €750 (=1), €750 up to less than €1,500 (=2), €1,500 up to less than €2,000 (=3), €2,000 up to less than €2,500 (=4), €2,500 up to less than €3,000 (=5), more than €3,000 (=6)”

- Regarding order effects I think that this is a major drawback and as such you should mention it in the conclusions rather than in a footnote.

We now say it not only in the experimental design (we think this should also be said there) but also in the Conclusion Section talking about limitations.

“Replication studies must show whether our findings are artifacts or systematical. For example, it is an open question whether order effects influenced our results.”

- Even though you do not directly answer the hypothesis I think you should clarify your result section so that is easier for the reader to understand the main results obtained from your study.

Yes, you are right. Results is a better description than “Data analysis”. Section 6 is not labeled as Results.

Other comments

- I think that mentioning the main results in the introduction would add to the paper but I respect that you think otherwise.

Thank you. Yes, there are different ways in the literature. � 

- Regarding the formula Fehr and Schmidt (1999) I would comment the purpose of having it there and that you are not using it further so that it is not misleading.

We now introduce the formula as follows:

“For illustration purposes, this will be presented formally (although the formula will not be used later in the paper):”

- I feel that you did not answer to my comment: “It may be the case that when receivers have a low endowment they do not trust senders because they may believe that they will try to even the payoffs”. I would add this as a possible explanation.

We think that this point is somewhat related to the definition issue we have written in the paper. This might be the case that we did not consider it in the revision (lost in thoughts). This was also in the old version of the paper: “To keep it simple, we stick to the terminology of Gneezy (2005) in this paper. However, we would like to point out that this dichotomy (honest vs. deception) could also be seen critically. For example, as Sutter (2009) correctly points out honest messages could also be classified as deception if one has the expectation that the receiver does not follow the message.”

And now, we added the following sentence:

“It should also be mentioned that receivers, who have less initial endowment than their opponents, might not trust the senders because the former could believe that the latter may try to even the payoffs as a fairness criterion.”

- It was difficult to understand this sentence of the introduction “Player 1 sends a message to player 2, which of the two options is supposedly financially advantageous for player 2. “ I think you cound add something like stating, explaining…after the comma.

We think that we missed a word in our sentence and made it hard to read. We added “indicating” after the comma (but stating was also fine to us). Thank you.

- Clarify in the introduction if the initial endowment is salient for all players.

In the Introduction, we describe the basic design along with the treatment conditions where we systematically vary in the endowment:

“In our extended Gneezy (2005) design, we provide either player 1 or 2 with an initial endowment of €10 in the treatment conditions. In accordance with Fehr and Schmidt (1999), we distinguish between monetary advantageous inequality and monetary disadvantageous inequality.”

Submitted filename: Response to Reviewers.docx

Click here for additional data file.

17 Dec 2021

Is there a link between endowment inequality and deception? – An analysis of students and chess players

PONE-D-21-22531R2

Dear Dr. Grüner,

We’re pleased to inform you that your manuscript has been judged scientifically suitable for publication and will be formally accepted for publication once it meets all outstanding technical requirements.

Within one week, you’ll receive an e-mail detailing the required amendments. When these have been addressed, you’ll receive a formal acceptance letter and your manuscript will be scheduled for publication.

An invoice for payment will follow shortly after the formal acceptance. To ensure an efficient process, please log into Editorial Manager at http://www.editorialmanager.com/pone/, click the 'Update My Information' link at the top of the page, and double check that your user information is up-to-date. If you have any billing related questions, please contact our Author Billing department directly at authorbilling@plos.org.

If your institution or institutions have a press office, please notify them about your upcoming paper to help maximize its impact. If they’ll be preparing press materials, please inform our press team as soon as possible -- no later than 48 hours after receiving the formal acceptance. Your manuscript will remain under strict press embargo until 2 pm Eastern Time on the date of publication. For more information, please contact onepress@plos.org.

Kind regards,

Natalia Jiménez, Ph.D. Economics

Academic Editor

PLOS ONE

Additional Editor Comments (optional):

Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Author

1. If the authors have adequately addressed your comments raised in a previous round of review and you feel that this manuscript is now acceptable for publication, you may indicate that here to bypass the “Comments to the Author” section, enter your conflict of interest statement in the “Confidential to Editor” section, and submit your "Accept" recommendation.

Reviewer #1: All comments have been addressed

**********

2. Is the manuscript technically sound, and do the data support the conclusions?

The manuscript must describe a technically sound piece of scientific research with data that supports the conclusions. Experiments must have been conducted rigorously, with appropriate controls, replication, and sample sizes. The conclusions must be drawn appropriately based on the data presented.

Reviewer #1: Yes

**********

3. Has the statistical analysis been performed appropriately and rigorously?

Reviewer #1: Yes

**********

4. Have the authors made all data underlying the findings in their manuscript fully available?

The PLOS Data policy requires authors to make all data underlying the findings described in their manuscript fully available without restriction, with rare exception (please refer to the Data Availability Statement in the manuscript PDF file). The data should be provided as part of the manuscript or its supporting information, or deposited to a public repository. For example, in addition to summary statistics, the data points behind means, medians and variance measures should be available. If there are restrictions on publicly sharing data—e.g. participant privacy or use of data from a third party—those must be specified.

Reviewer #1: (No Response)

**********

5. Is the manuscript presented in an intelligible fashion and written in standard English?

PLOS ONE does not copyedit accepted manuscripts, so the language in submitted articles must be clear, correct, and unambiguous. Any typographical or grammatical errors should be corrected at revision, so please note any specific errors here.

Reviewer #1: Yes

**********

6. Review Comments to the Author

Please use the space provided to explain your answers to the questions above. You may also include additional comments for the author, including concerns about dual publication, research ethics, or publication ethics. (Please upload your review as an attachment if it exceeds 20,000 characters)

Reviewer #1: (No Response)

**********

7. PLOS authors have the option to publish the peer review history of their article (what does this mean?). If published, this will include your full peer review and any attached files.

If you choose “no”, your identity will remain anonymous but your review may still be made public.

Do you want your identity to be public for this peer review? For information about this choice, including consent withdrawal, please see our Privacy Policy.

Reviewer #1: No

12 Jan 2022

PONE-D-21-22531R2

Is there a link between endowment inequality and deception? – An analysis of students and chess players

Dear Dr. Grüner:

I'm pleased to inform you that your manuscript has been deemed suitable for publication in PLOS ONE. Congratulations! Your manuscript is now with our production department.

If your institution or institutions have a press office, please let them know about your upcoming paper now to help maximize its impact. If they'll be preparing press materials, please inform our press team within the next 48 hours. Your manuscript will remain under strict press embargo until 2 pm Eastern Time on the date of publication. For more information please contact onepress@plos.org.

If we can help with anything else, please email us at plosone@plos.org.

Thank you for submitting your work to PLOS ONE and supporting open access.

Kind regards,

PLOS ONE Editorial Office Staff

on behalf of

Dr. Natalia Jiménez

Academic Editor

PLOS ONE