# Socioeconomic Distance and the Selectivity in Punishment and Reward

Irving Argaez Corona, Béatrice Boulu-Reshef, Jean-Christophe Vergnaud

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Irving Argaez Corona, Béatrice Boulu-Reshef, Jean-Christophe Vergnaud. Socioeconomic Distance and the Selectivity in Punishment and Reward. 2025. hal-05368602

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# Socioeconomic Distance and the Selectivity in Punishment and Reward

Irving Argaez Corona<sup>a</sup>; Béatrice Boulu-Reshef<sup>b</sup>; Jean-Christophe Vergnaud<sup>ac</sup>

<sup>a</sup>Centre d'Économie de la Sorbonne (CES), Université Paris 1, France

<sup>b</sup>CY Cergy Paris Université (THEMA), France

<sup>c</sup>Centre National de la Recherche Scientifique (CNRS), France

## Abstract

Do we punish distant others more harshly and reward close others more readily? We study these decisions in an iterated online Die-under-the-Cup (DUTC) task with $n = 720$ participants randomly assigned to fixed roles: Die-rollers (P1) and Observers (P2). Over 24 rounds, each P2 is paired with two 12-round blocks of P1s-one socially close and one socially distant—under one of three treatments: Punishment, Reward, or Mixed. P2 privately observes both P1's true and reported values, and can apply a €2 penalty or a +€2 reward that does not affect P2's own payoff. Social closeness is modelled through socioeconomic status (SES) using (1) an objective measure based on average income in the participant's locality of residence and (2) a subjective measure based on self-reported income relative to the locality's average. We construct an observer-level proxy for suspicious reporting using excess self-serving reports relative to fair odds within the 12 reports seen by P2 per SES and test whether social closeness moderates enforcement. Findings show that punishment increases with the suspicion proxy but is weaker for close counterparts, while rewards are granted more often for non-suspicious reports. Third-party penalties and rewards are selective across SES: at comparable suspicion levels, low-SES counterparts are punished more than medium/high-SES counterparts, yet they also receive more rewards for non-suspicious reports. Moreover, we observe that the objective measure of closeness is linked to overall leniency toward close counterparts, whereas the subjective measure shifts reactions to the suspicion proxy: weaker for close counterparts and stronger for distant ones. Overall, our study reveals that counterpart SES shapes responses to reported outcomes.

**Keywords** Social closeness; social distance; observability; suspicious reporting; socioeconomic status; punishment; reward; income levels.

**JEL codes** C31 C73 C91 D71 D91

This project benefitted from funding from the *Centre d'Économie de la Sorbonne (CES)*'s 2025 campaign. The project received approval from the Institutional Review Board of Paris School of Economics (decision 2025-030). The pre-registered protocol can be found in this link, as well as in the Appendix, for peer-review purposes. We warmly thank **Maxim Frolov**, computer engineer at *Laboratoire d'Economie Expérimentale de Paris (LEEP)*, for his support in programming the experiment and organising the sessions.
# 1 Introduction

Individual decisions to cheat often transcend personal consequences and impact broader social outcomes. Evidence suggests that seeing similar others cheat can increase dishonesty among observers (Bicchieri et al., 2022; Dimant, 2019; Jordan et al., 2024; Kang et al., 2021). In this sense, this paper addresses two questions and tests them experimentally: (1) when observers evaluate reported outcomes that differ in how suspicious they look, do they punish suspicious reports and reward non-suspicious reports?, and (2) does social closeness shape these reactions? We measure suspicion with an Observer-level proxy for cheating, vary social closeness within participants using objective and subjective measures of socioeconomic status (SES), and estimate how punishment and reward respond to the suspicion proxy when paired with close versus distant pairs.

Prior research shows that punishment choices depend on perceived harm and inequality and are shaped by in-group preferences (Bone et al., 2016; Deutchman et al., 2021; Rullo et al., 2024). Recent papers document that support for sanctions is heterogeneous, with in-group loyalty reducing willingness to sanction even under clear norm violations (Loustau et al., 2024; van Oosten, 2025), especially when sanctions threaten group status (Hershcovis et al., 2017; Leib et al., 2021; Rullo et al., 2019). At the same time, self-image concerns and the wish to appear trustworthy deter dishonesty (Barranti et al., 2016; Blanken et al., 2015; Fischbacher and Föllmi-Heusi, 2013; Mazar et al., 2008), with internalised norms operating most strongly within in-groups (Grigoryan et al., 2023; Kimbrough and Vostroknutov, 2016). These findings motivate testing whether social closeness alters how Observers react to suspicious versus non-suspicious reports.

The study examines these questions in a repeated online Die-under-the-Cup (DUTC) task where Observers (P2) rotate with 24 counterparts in two 12-round blocks, one with socially close and one with socially distant counterparts. In the setting, Observers see the true and the reported values from Die-rollers (P1), with true values being anonymous to the experimenters. Participants are randomly assigned to one of three treatments: *Punish* (P2 may impose a -2€ penalty to P1), *Reward* (P2 may provide a +2€ reward to P1), or *Mixed* (P2 is randomly assigned to one of three possible options: observe, punish, or reward). The design allows to capture responses to both suspicious and non-suspicious reports, as well as comparisons across SES tiers (i.e., low, medium, high).

We construct an Observer-level proxy for suspicious reporting by comparing, within each 12-round block, the frequency of each reported face to the uniform benchmark. We then weight any excess by whether the face is payoff-maximising or payoff-reducing, assigning a round-level suspicion signal. Moreover, we make Observers' payoffs independent to their decisions to punish or reward, in order to isolate loss-recovery or reciprocity motives in their decisions.

Social closeness is defined via socioeconomic status (SES) using an objective measure (average income in the participant's department of residence) and a subjective measure (self-reported income relative to the departmental average). This logic follows existing evidence on how inequality and SES similarity shape interpersonal judgement and behaviour (Elbæk et al., 2023; Martinangeli and Martinsson, 2020; Moss et al., 2023)).
The papers' contributions are threefold. First, we introduce a transparent, observer-level suspicion proxy that preserves the DUTC's inference logic while allowing clean tests of how Observers react to suspicious versus non-suspicious reports. Second, we analyse third-party sanctions and rewards jointly, rather than focusing on punishment alone. Third, we identify how socioeconomic closeness moderates these reactions using both objective and subjective measures of SES.

Our results show that decisions to punish and reward are robustly associated with both the suspicion proxy and the counterpart's socioeconomic context. Punishment rises with suspicion but is attenuated for objectively close counterparts, consistent with in-group leniency. Moreover, punishment is also socioeconomically selective as low-SES counterparts are punished more than medium or high-SES ones for the same level of suspicion. Conversely, Observers reward non-suspicious reports more often, with low-SES counterparts receiving more rewards and high-SES ones receiving the least. We also find that subjective closeness does not shift average punishment or reward levels, but instead changes sensitivity to suspicion, with weaker reactions for close counterparts and stronger for distant ones. Overall, our study shows decisions to punish and reward are selective, shaped jointly by suspicions of cheating and by social closeness to the counterparts.

The paper proceeds as follows: Section 2 elaborates on the existing literature, the theoretical framework for the paper and its contributions. Section 3 presents the experimental design and procedures. Section 4 reports the descriptive statistics and Section 5 reports the results. Finally, Section 6 concludes.

# 2 Theoretical background and related literature

This study takes from and contributes to three key areas of the literature. In this section, we outline the theoretical foundations and empirical findings that inform our approach, where our study sits and how this theoretical background helps in testing our hypotheses.

## 2.1 Inferring cheating in the DUTC paradigm

A central challenge in dishonesty research is that, by design, many paradigms do not adjudicate cheating at the individual level. This is the case with the Die-under-the-Cup (DUTC) task, where participants privately observe a die outcome and self-report for payoff; cheating is therefore inferred statistically from how reported outcomes deviate from the uniform distribution. This logic is used throughout the DUTC literature: truthful behaviour produces an approximately uniform distribution of reports and systematic excess of payoff-maximising reports signals dishonesty in aggregate terms (Fischbacher and Föllmi-Heusi, 2013; Kocher et al., 2018).

Inferential estimation is common to lab and online applications of the DUTC, where cheating is almost always inferred from report distributions (Hermann and Ostermaier, 2018; Kroher and Wolbring, 2015; Siniver et al., 2022). Moreover, evidence proves that this feature upholds even across modified versions of the paradigm, either by changing feedback (Kroher and Wolbring, 2015), inducing competition settings (Benistant et al., 2022) or introducing sanction schemes (Siniver et al., 2022). These adaptations can inflate or reduce over-reporting, whilst preserving the core logic that cheating is inferred from distribution
and not from personalised behaviour.

While this approximation has made the DUTC a leading paradigm to experimentally detect dishonesty, it constrains how cheating is interpreted. A complementary literature contrasts aggregate with individual detection, showing that DUTC paradigms identify cheating only at the group level, whereas individual-verification and anomaly-scoring approaches can flag specific cheaters, thereby corroborating, rather than replacing, DUTC-based inference (Heyman et al., 2020; Kaluza et al., 2012). These studies suggest that aggregate and individual approaches illustrate different facets of dishonesty and that careful, context-sensitive inference remains necessary.

Our design follows this logic. True rolls are shown to P2 and subsequently deleted from the master data, hence not observed by experimenters. We therefore construct an Observer-level, signal-based proxy for suspicious reporting by flagging excess frequency on self-serving faces relative to fair odds within each 12-report block. We then study how penalties and rewards respond to this proxy and whether socioeconomic closeness moderates these responses. This preserves the DUTC's distributional inference while enabling clean tests of Observer behaviour across socioeconomic contexts.

## 2.2 Behavioural responses: punishment and reward

Evidence shows that group boundaries shape punitive and reward choices. Observers punish out-group violators more and are more lenient toward in-group members (Loustau et al., 2024; Van Assche et al., 2020); in-group favouritism and out-group discrimination both enter norm responses (Schiller et al., 2014). Enforcement also reflects concerns about harm and inequality (Leibbrandt et al., 2023) and is stronger when group outcomes are salient (Windrich et al., 2024). Across settings, social conditions, power dynamics, and background heterogeneity shift enforcement thresholds (Hershcovis et al., 2017; Kocher et al., 2012; Molho et al., 2024; Winter and Zhang, 2018). The common result is asymmetry: the same transgression draws harsher action against out-groups than in-groups (Rullo et al., 2019,2; Van Assche et al., 2020; Winter and Zhang, 2018).

However, punishment is only one lever, as rewards can complement or even substitute sanctions. In public-goods environments, punishment opportunities raise contributions, and well-designed rewards can stabilise cooperation; which lever dominates depends on the strategic context and prevailing norms (Kocher et al., 2012). Outside the lab, enforcement presence and reward salience curb dishonesty (Kaushik et al., 2021; Rantakari, 2023). Group-level reward schemes can outperform individual or mixed schemes by promoting cooperation (Ladley et al., 2015).

Our study builds directly on these insights and tackles enforcement across social distance as a central challenge in real-life interactions. First, Observers in our design see the Die-roller's report and decide whether to punish (-2€) or reward (+2€) with no impact to their own payoffs. By removing reciprocity, the design not only isolates the observed behaviour, but also eliminates personal consequences on decisions. Second, we focus on social closeness by varying socioeconomic (dis)similarity between participants. This allows us to propose a model that combines punishment and reward in a single enforcement framework across socioeconomic differences, all while preserving a clean research environment that allows for anonymity from the researchers.
## 2.3 Socioeconomic status and selective attitudes

A large body of work shows that socioeconomic status (SES) is not merely a background descriptor but a significant social mechanism: it shapes self-concept, moral judgment and the way individuals relate to others. Socialisation between individuals with different SES produces distinct behaviours and social appraisals (Manstead, 2018), as people attach substantial psychological importance to SES-linked identities (Easterbrook et al., 2020). SES also organises social perceptions and interactions in different ways: Kraus et al. (2011) show that cues on social class systematically alter cognition and interpersonal behaviour; Chae et al. (2022) claim that resource scarcity fosters in-group favouritism, often at the expense of fairness toward outsiders; while Renger et al. (2024) find SES divergence transforms how norm violations are perceived and confronted, mainly related to unequal treatment towards lower-income individuals.

In this sense, Hauser et al. (2021) shows that when income distribution is unknown, observers tend to reward the rich for large, absolute contributions and punish the poor for small ones; when inequality is revealed, judgments flip to relative standards-punishing the rich for low percentage contributions and rewarding the poor for high percentage ones. More generally, identical transgressions targeting wealthy versus poor agents are judged through different lenses: poorer targets are often seen as less immoral for the same violation and as more prosocial for the same good deed (Weiner and Laurent, 2021). Similarly, evidence on civic honesty is mixed but equally status-driven: a lost-wallet experiment correlates higher income with lower civic honesty (Du et al., 2020), a large cross-national survey suggests that lower SES can go along with stronger moral concerns, challenging simple "low-SES, low morality" stereotypes (Elbæk et al., 2023), and SES ranking and perceived inequality causally shape redistribution attitudes through appraisals of fairness (Brown-Iannuzzi et al., 2021).

Furthermore, selective enforcement depends on who holds the power to sanction. For instance, Pansini et al. (2018) analyse class-segregated settings where the rich can punish the poor, finding that the rich cooperate less, punish more and end up earning roughly twice as much as the poor. These patterns echo broader preferences skewed against lower-income individuals, while recognising how everyday interactions and institutions reproduce exclusion (Blokland, 2012). They also explain why many people prefer to self-identify as “middle class” even when objective indicators place them low in the economic ladder (Bussolo et al., 2020).

This literature yields clear and testable implications for our setting. First, if distance reduces empathy and heightens discriminatory patterns, socioeconomic distance should amplify punishment when an observer perceives suspicious and payoff-maximising reports. Second, socioeconomic closeness should amplify rewards when suspicion is low or absent, and potentially elevate baseline rewarding even when signals are neutral. Our design models these predictions using an observer-centred approach (from DUTC report distributions) and exogenous variation in SES closeness/distance between players.

## 2.4 Hypotheses and contributions

Guided by the existing literature, we evaluate two hypotheses in a single framework:
• H1: **Punishment** × **Distance**: Observers punish suspicious reports more readily when the counterpart is socially distant.

• H2: **Reward** × **Closeness**: Observers reward non-suspicious reports more readily when the counterpart is socially close.

Because the suspicion signal is fixed by what P2 observed, differences by SES are interpretable as selective enforcement across social boundaries.

Our paper advances the literature in three ways:

(1) **A proxy to capture suspicious cheating at the Observer-level.** We build a continuous, round-level proxy at the Observer-level. We flag statistically unusual spikes in specific reports within each Observer×SES cell (12 rounds), weight them by the marginal payoff of the reported die value (upweighting payoff-maximising faces, down-weighting payoff-reducing ones) and attach the resulting score to that Observer's round. This retains the DUTC's aggregate inference, but shifts the signal down to the level of what each Observer actually sees in their respective treatment condition.

This proxy allows us to move beyond the traditional sample-level measure of cheating in the DUTC, while incorporating the strategic relevance of reports by weighting excess frequency with marginal payoffs. The ultimate objective is to propose a model producing a continuous signal varying across Observers, SES pairings and relevant rounds, while providing a continuous signal of suspicious cheating.

(2) **A two-side, stake-free third-party punishment/reward framework.** We analyse punishment and rewards as two sides of the same mechanism, mapping both onto a common scale and administering them by Observers whose own payoffs are unaffected. This design isolates responses to suspicious reports from motives linked to self-interest (e.g., retaliation, loss recovery, reciprocity).

(3) **Socioeconomic selectivity.** We manipulate socioeconomic closeness/distance between participants, objectively (by average income level in departments of residence) and subjectively (by personal income in comparison to departmental average), and test whether the same suspicion signal elicits different responses toward close vs. distant counterparts.

# 3 Experimental design and procedures

The experimental setting consists of three tasks: (1) a socioeconomic survey, (2) an online Die-Under-the-Cup (DUTC) task, and (3) the Moral Identity (MIS) scale. We ran the experiment online with three treatment conditions: Punishment (Treatment 1), Reward (Treatment 2) and Mixed (Treatment 3). In the following sections we provide a detailed overview of the experimental design and its tasks.

## Participant recruitment and stratification

We ran the study online with participants from the Laboratory of Experimental Economics of Paris (LEEP). At invitation, we pre-screened by postal code to map each registrant to a department of residence and its corresponding SES tier (Low, Medium, High), using data from the French National Institute of
*Statistics and Economic Studies (INSEE)*. Invitations were stratified by tier with tier-specific quotas to keep the pool balanced and ensure even pairings. Department coverage and tier assignment are reported in Appendix Table 9; a geographic visualisation appears in Figure 7.

Participant allocation followed a two-step plan: we first filled the *Mixed* treatment, as this was the largest and most complex condition (n = 432), then directed additional recruits to the *Punish* (n = 144) and *Reward* (n = 144) treatments. Participant roles (P1, P2) were randomised at login. Matching was organised in subsessions that included exactly two SES tiers (e.g., Low & Medium or Low & High), to ensure exact pairing cells within each subsession. For example, in a Low-Medium SES subsession, a Low-SES Observer (P2: Low) completed one 12-round block with 12 Low-SES Die-rollers (P1: Low; socially close) and one 12-round block with 12 Medium-SES Die-rollers (P1: Medium; socially distant). For a visual representation of SES-based pairs in the subsessions, see Figure 1.

<figure><img src="image_1.png" /><figcaption>Figure 1: Pairing by subsession (two-tier SES matching)</figcaption></figure>

Solid line = same-tier (close pairings); dashed line = cross-tier (distant pairings). Shaded squares denote P2 (Observers), the unit of analysis. Each P2 completes 12 close and 12 distant rounds per subsession.

## Task 1. Socioeconomic questionnaire and participant categorisation

Participants completed a socioeconomic questionnaire covering demographics (age, gender, marital status, education, occupation) and socioeconomic information (personal monthly net income, partner's income, weekly working hours, housing status, credit situation and enrolment in social security programmes). For income-related questions, participants selected one of five ordered brackets ranging from 1 (under 1,000€) to 5 (over 6,000€), plus a non-applicable option. Given that a substantial share of participants were non-working students (and to a lesser extent unemployed individuals) who reported having no income, we use partner and household income as proxies.

### Objective social distance

Objective SES is constructed from average monthly income at the departmental level. At the time of recruitment, we observe only participants' post codes (not personal income), therefore, we anchor SES tiers to INSEE's 2021 *niveau de vie médian* (median disposable income per consumption unit) per month, at the departmental level INSEE Références (2021). Tiers are anchored to national reference points:

* **Low SES:** departmental median < 1,993€ (national median);

* **Medium SES:** 1,993€ < departmental median < 2,477€;

* **High SES:** departmental median > 2,477€ (top-income departments: Paris and Hauts-de-Seine).
This location-based SES captures the income environment of where participants live. Objective social distance is then defined at the pair level between Observer $P_2$ and Die-roller $P_1$:

$$ \text{distance}_{P_2 P_1} = |\text{SES}^{\text{obj}}_{P_2} - \text{SES}^{\text{obj}}_{P_1}| \in \{0, 1\}, $$

where 0 indicates same tier (socially close) and 1 different tiers (socially distant). For a comprehensive overview of the departments participants were recruited from and their categorisation by SES level, see Table 9.

## Subjective social closeness

We construct a three-tier subjective SES from the income brackets reported in Task 1, mirroring the logic used for objective closeness. Let player_revenue be the participant's self-income bracket (1–5; 6 = no income). We define:

$$ \text{SES}^{\text{subj}} = \begin{cases} \text{Low} & \text{if } \text{player\_revenue} \in \{1, 6\}, \\ \text{Medium} & \text{if } \text{player\_revenue} = 2, \\ \text{High} & \text{if } \text{player\_revenue} \in \{3, 4, 5\}. \end{cases} $$

We then run adjustments for participants with no personal income (player_revenue = 6), using partner income and, if needed, household income brackets:

$$ \text{SES}^{\text{subj}} = \begin{cases} \text{High} & \text{if partner bracket } \in \{4, 5\}, \\ \text{High} & \text{if partner } = 6 \text{ and household } \in \{4, 5\}, \\ \text{Medium} & \text{if partner } = 3, \\ \text{Medium} & \text{if partner } = 6 \text{ and household } = 3, \\ \text{Low} & \text{otherwise.} \end{cases} $$

Finally, we compute the subjective closeness indicator by comparing it to the participant's objective SES tier from their department of residence (player_tier ∈ {Low, Medium, High}):

$$ \text{socially\_close\_subj} = \begin{cases} 1 & \text{if } \text{SES}^{\text{subj}} = \text{player\_tier}, \\ 0 & \text{if } \text{SES}^{\text{subj}} \neq \text{player\_tier}, \end{cases} \quad \text{and} \quad \text{socially\_distant}^{\text{subj}} = 1 - \text{socially\_close}^{\text{subj}}. $$

This procedure yields a clean subjective SES based primarily on personal income, with transparent partner/household reclassification only for respondents reporting no personal income, and a binary subjective closeness measure by matching subjective and objective tiers.

## Socioeconomic status in experimental research

Modelling social closeness through socioeconomic status is grounded in both theoretical and empirical reasoning. A growing body of research identifies it as a powerful and multidimensional indicator of social identity and perceived interpersonal closeness (Easterbrook et al., 2019; Kraus et al., 2011; Manstead,
2018). Moreover, SES encompasses objective indicators, such as income, employment and education, as well as subjective dimensions, including perceptions, emotions, attitudes and moral values.

Using socioeconomic closeness as a proxy for social closeness allows us to analyse behavioural responses when cheating is committed by individuals from different socioeconomic backgrounds. In this sense, Kraus et al. (2011) found that income differences create strong in-group identity, particularly among working and middle-class individuals, which define their sense of belonging in opposition to out-groupers. This is further studied from a nationality-based perspective in Magni (2021), who show that greater inequality relates to greater favouritism towards nationals over immigrants in resource distribution. Similarly, Du et al. (2020) found that in societies with high perceptions of systemic income inequality, social norm enforcement tends to erode.

The literature presents divergent views regarding the effects of income inequalities for honesty: Chae et al. (2022) argue that resource scarcity increases in-group favouritism and induces group loyalty, hindering honesty. Rubin et al. (2014) show that individuals in lower income brackets tend to engage in in-group favouritism as a compensatory mechanism for their unfavourable position. Conversely, Elbæk et al. (2023) show that individuals with lower SES show stronger moral identity and prosocial intention, challenging the assumptions that low-income relates to moral decline. This is supported in Martinangeli and Martinsson (2020), who reveal that when observing peer behaviour, low-income individuals become more norm-compliant when their in-group behaves honestly, whereas high-income individuals are more likely to justify dishonesty when their peers cheat.

We deem this analysis relevant in light of rising income disparities around the globe and the polarisation that societies increasingly experience. Our interest is to provide a novel perspective that links objective and subjective measures of closeness to suspicions of cheating in the DUTC.

## Task 2. Online Die-Under-the-Cup (DUTC) task

Participants complete 24 consecutive rounds of a DUTC in fixed, randomly assigned roles:

* **Die-roller (P1):** privately rolls a die, observes the true outcome value, and registers a value for payment.

* **Observer (P2):** observes both the true outcome value and P1's registered value and, depending on the treatment, may apply a -2 penalty, a +2 reward, or simply observe; P2 then registers their own payoff.

Payoffs equal the registered die value in euros, except that a 6 yields 0. With a fair die each outcome occurs with probability 1/6, so under truthful reporting the expected mean is

$$ \frac{1 + 2 + 3 + 4 + 5 + 0}{6} = 2.5. $$

One of the 24 rounds is randomly selected for payment at the end of the task.

Each round proceeds as follows:
1. **P1 private roll.** A virtual die appears on P1's screen. When P1 clicks *Roll*, the outcome is generated locally using the browser's cryptographic randomness; the true value $k \in \{1, \dots, 6\}$ is shown to P1.

2. **P1 registration.** P1 enters a value to be used for payment.

3. **P2 observation.** P2 sees the true value and P1's registered value, applies the treatment-specific choice (penalise or reward), and then registers their own payoff for the round.

4. **Data handling.** After the round, the true outcome is not retained in the research dataset. Server logs store session metadata (session ID, round, treatment, role), registered values for payment, and P2's decision (punish/reward). True outcomes are not accessible to experimenters *ex post*.

Before each round, P2 is shown the counterpart's department-level average monthly income and its SES tier (Low/Medium/High), making socioeconomic distance salient without revealing identities.

## Construction of the proxy for suspicion of cheating

Because experimenters do not observe P1's true outcome values, individual cheating cannot be directly identified after the experiment. We therefore construct a round-level suspicion signal that increases when two conditions jointly hold: (1) the value registered in the round is over-represented relative to a uniform benchmark and (2) that value is payoff-maximising for P1.

### Setting the suspicion proxy.

Each Observer (P2) sees 24 registered values in total, split into two 12-round blocks: one with socially close counterparts and one with socially distant counterparts. Under truthful reporting, each face should appear with probability 1/6, so the expected count per face in a 12-round block is 2. Systematic counts above this benchmark indicate over-representation and are treated as suspicious. The proxy converts this abnormality into a round-level signal and weights it by payoff consequences (faces 4-5 are payoff-maximising; 1, 2, and 6 are payoff-reducing; 3 is near neutral). In what follows we detail step-by-step the proxy's construction:

**Step 1: Count recorded faces within each block.** For each Observer $i$, block $s \in \{\text{close}, \text{distant}\}$, and value $k \in \{1, \dots, 6\}$, let

$$n_{ik}^{(s)} = \sum_{r=1}^{12} 1\{\text{recorded\_value}_{ir}^{(s)} = k\}$$

be the number of times value $k$ was registered in the 12 rounds of block $s$.

**Step 2: Compute excess frequency (over the uniform benchmark)** Translate excess concentration into a unit-interval share:

$$b_{ik}^{(s)} = \begin{cases} \frac{n_{ik}^{(s)} - 2}{n_{ik}^{(s)}}, & \text{if } n_{ik}^{(s)} > 2, \\ 0, & \text{if } n_{ik}^{(s)} \le 2. \end{cases}$$
**Step 3: Attach the excess to the current round** In round $r$ of block $s$, let $k(r)$ denote the registered value. The round-level abnormality term is

$$E_{ir}^{(s)} = e_{i, k(r)}^{(s)}.$$

**Step 4: Weighting by incentives (payoff alignment).** Reports map into payoffs in euros (reports 1–5 pay 1–5€; reporting 6 pays 0€). To align the proxy with payoff-motivated misreporting, we weight by the marginal payoff consequences of each value:

$$S_{ir}^{(s)} = \sum_{k=1}^{6} w_k b_{ik}^{(s)} x_{ir}^{(s)}(k), \quad (w_1, w_2, w_3, w_4, w_5, w_6) = (-1.5, -0.5, 0.5, 1.5, 2.5, -2.5).$$

Because only the reported value enters at round $r$, $S_{ir}^{(s)}$ reduces to the weight for that value times its excess share. Positive values indicate unusual concentration of payoff-maximising reports (4 or 5); negative values indicate unusual concentration of payoff-reducing reports (1, 2, or 6); values near zero are consistent with uniform play.

For instance, if in the 12 distant rounds for Observer $i$ the value 5 appears 5 times, then

$$e_{i5}^{(\text{distant})} = \frac{5}{12} - \frac{1}{6} = 0.25,$$

so any distant round where 5 is registered has

$$S_{ir}^{(\text{distant})} = 2.5 \times 0.25 = 0.625 > 0.$$

Thereby reflecting a suspicious report in that particular round.

On the contrary, if in the 12 close rounds the value 1 appears 4 times, then

$$e_{i1}^{(\text{close})} = \frac{4}{12} - \frac{1}{6} = 0.1667,$$

and a close round registering 1 yields

$$S_{ir}^{(\text{close})} = -1.5 \times 0.1667 \approx -0.25.$$

Thereby reflecting an unsuspicious report in that particular round.

## Treatment conditions

The experiment has three treatment conditions. At each round, Observers know: (1) the average monthly income in their department of residence, (2) the average monthly income in the Die-roller's department of residence, (3) the income tier of both departments, and (4) the national average monthly income in France, as a benchmark.

Die-rollers know that P2 can see both the true die outcome and the value they register for payment, and that P2 may have the ability to punish or reward depending on the assigned condition. However, they are not told the Observer's department of residence (proxy for social distance), the Observer's punish or reward decisions, nor their own round-level earnings until the experiment ends.
This serves two purposes: by withholding information about the Observer, we isolate Die-rollers' cheating behaviour from reputational concerns or reactive feedback, allowing for a cleaner measure of their suspicious cheating; and it models a realistic norm-enforcement scenario for Observers.

## Treatment 1: Punishment

Player 1 (P1) rolls a die, obtains the true value $Y_{i,r}^{\text{true}} \in \{1, 2, 3, 4, 5, 6\}$ and reports a value $Y_{i,r}^{\text{rep}}$.

Player 2 (P2) observes both $Y_{i,r}^{\text{true}}$ and $Y_{i,r}^{\text{rep}}$, and decides whether to apply a -2€ penalty from P1's payoff:

$$ \text{Payoff}_{i,r} = \max(0, Y_{i,r}^{\text{rep}} - 2) $$

P2 then registers their own payoff $Y_{j,r}^{\text{rep}}$.

The Observer's decision to punish is independent of whether P1 cheated or not.

## Treatment 2: Reward

P1 proceeds as in Treatment 1.

P2 observes both $Y_{i,r}^{\text{true}}$ and $Y_{i,r}^{\text{rep}}$, and decides whether to apply a +2€ reward to their payoff:

$$ \text{Payoff}_{i,r} = \max(0, Y_{i,r}^{\text{rep}} + 2) $$

The Observer's decision to reward is also independent of whether P1 cheated or not.

## Treatment 3: Mixed

P1 proceeds as in Treatment 1.

P2 is informed that there are three possible conditions they can be assigned to:

* **Punish:** Can apply a -2€ penalty to P1's payoff.

* **Reward:** Can apply a +2€ reward to P1's payoff.

* **Observer:** Only observes P1's behaviour.

At the start of the game, Observers are informed of the conditions they have been assigned to and that they will stay in this condition for the entirety of the game. They are also informed that this information will not be disclosed to P1.

Die-rollers are informed of the three possible conditions for Observers and that they will be randomly paired with 24 participants playing in one these roles. However, they are not informed of which type of Observer they are being paired with.

This treatment allows us to estimate anticipatory effects on whether the mere possibility of sanction or reward (as opposed to certainty) deters cheating or encourages honesty. Furthermore, it provides a cleaner test of social selectivity in enforcement, as any differences in P2's behaviour by social distance are less confounded by P1's strategic adaptation to a fixed regime.
## Task 3. Moral Identity Scale (MIS)

We administered the Moral Identity Scale Aquino and Reed (2002) to capture stable individual differences in the centrality of moral traits to the self-concept. The instrument comprises two subscales—Internalisation (moral traits as part of one's self-view) and Symbolisation (expressing moral traits outwardly)—with items rated on a 1–10 scale (1 = “not at all,” 10 = “very much”). Traits such as *honest, fair* and reverse-coded antonyms (e.g., *ruthless, selfish*) were included. The MIS was administered after the DUTC to avoid priming moral concerns during enforcement decisions.

Because MIS captures broad, trait-like heterogeneity that can absorb meaningful between-subject variation in enforcement, including it as a main regression control risks over-controlling and complicating interpretation of treatment and closeness effects. We therefore decided to exclude this variable from our analyses.

## Experimental procedures

The experiment was run online in July of 2025. We recruited 780 volunteers, after applying pre-specified exclusions for incomplete participation, we excluded 60 participants, yielding a final sample of *n* = 720 participants (60% female), with a mean age of 28.6 years (SD = 9.6). The pool consisted mainly of students (41.5%) and employed individuals (39%); see Appendix Tables 5 and 6 for education and occupation details. Average earnings were €6.14 (SD = €4.88), including a €3 show-up fee.

Participants were assigned at login to one of three session-level treatments: *Punish* (*n* = 144), *Reward* (*n* = 144), or *Mixed* (*n* = 432). Each participant completed 24 rounds, for a total of 17,280 round-level observations: 3,456 in *Punish* (144 × 24), 3,456 in *Reward* (144 × 24), and 10,368 in *Mixed* (432 × 24).

Round-level observations are not independent because each participant contributes 24 decisions. Accordingly, all inference uses cluster-robust standard errors at the participant level. For P2 decisions, standard errors are clustered by *Observer*; for models of P1 reporting, they are clustered by *Die-roller*. As a robustness check, we also report specifications with two-way clustering by P1 and P2 when both actors’ histories may induce dependence. Regression tables report the total number of round-level observations and the number of clusters used for inference.

# 4 Descriptive statistics

## 4.1 Die-roll reports and potential cheating propensities

Figure 2 shows the distribution of Die-rollers’ reported outcomes by treatment. As in standard DUTC settings, reports of 5 are over-represented relative to the 16.7% uniform benchmark, reports of 1, 2, and 6 are under-represented, and 3–4 sit closer to uniform. For inference, we collapsed to participant–treatment shares (one observation per P1×Treatment) and ran OLS of the share of 5s on treatment dummies with standard errors clustered by participant. This yields *N* = 360 cells (Punish: 72, Reward: 72, Mixed: 216). A joint equality test gives $F(2, 359) = 0.70, p = 0.497$; pairwise margins: Reward-Punish $\Delta = -0.023$, $p = 0.565$; Mixed-Punish $\Delta = -0.038, p = 0.245$; Reward-Mixed $\Delta = 0.014, p = 0.657$.
Within each treatment, we tested the mean share of 5s against 1/6 using one-sample regressions with participant-clustered errors. Estimated means confirm excess of payoff-maximising reports in all treatments: Punish $\hat{\mu} = 0.292$ (72 clusters; $F(1, 71) = 18.39, p = 0.000$); Reward $\hat{\mu} = 0.269$ (72; $F(1, 71) = 12.28, p = 0.000$); Mixed $\hat{\mu} = 0.254$ (216; $F(1, 215) = 34.54, p < 0.001$).

<figure><img src="image_2.png" /><figcaption>Figure 2: Die-roll reports by treatments (P1)</figcaption></figure>

Figure 3 disaggregates P1 reports by SES, showing that trends persist: excess reports of 5, fewer reports of 1, 2 and 6. For inference, we collapsed to participant-level shares (one P1×SES observation per participant) and regressed the share of 5s on SES indicators with standard errors clustered by participant ($N = 8,640$ round-level observations mapped into 360 clusters). A joint test across tiers gives $F(2, 359) = 4.89, p = 0.008$. Relative to High-SES, Low-SES ($\Delta = -0.091, p = 0.003$) and Medium-SES ($\Delta = -0.083, p = 0.009$) report fewer 5s. One-sample clustered tests against 1/6 show that each tier still exceeds the uniform benchmark (Low: $F(1, 119) = 37.67, p < 0.001$; Medium: $F(1, 119) = 15.47, p < 0.001$; High: $F(1, 119) = 14.23, p < 0.001$). Moreover, an ordered trend (High= 1, Medium= 2, Low= 3) indicates a decline in reports of 5 as SES decreases: $\hat{\beta} = 0.0457$ (two-sided $p = 0.003$). In short, the spike in payoff-maximising reports is present for all SES groups and is strongest among High-SES participants (see also Alfonso-Costillo et al. (2022); Fischbacher and Föllmi-Heusi (2013); Hermann and Ostermaier (2018); Kocher et al. (2018)).
<figure><img src="image_3.png" /><figcaption>Figure 3: Die-roll reports by SES (P1)</figcaption></figure>

Figure 4 plots round-by-round mean P1 gains by treatment, with a reference line at the truthful benchmark (2.5). Mean gains exceed 2.5 in all treatments (Punish = 2.962, Reward = 2.898, Mixed = 2.832; each *p* < 0.001 from clustered one-sample tests), consistent with excess in payoff-maximising reports. Using round-level data with participant-clustered errors, mean gains do not differ across treatments (*F*(2, 359) = 0.70, *p* = 0.500), nor do trends diverge systematically over rounds. This suggests treatment differences—if any—operate via the composition of reported values rather than sustained shifts in average earnings.

Because true P1 outcomes are anonymous to researchers, suspicion is inferred by combining these gain patterns with report distributions and P2 decisions. Intuitively, if P2s persistently penalised high reports, mean gains would fall below 2.5 in Punish; if P2s persistently rewarded moderate reports, mean gains would sit above 2.5 in Reward. The similarity across panels indicates no net punishment or reward effect on average earnings over time. The high similarity in both graphs shows no evidence of a net punishment or net reward effect on average P1 earnings across rounds.

<figure><img src="image_4.png" /><figcaption>Figure 4: P1 mean earnings by treatment across 24 rounds</figcaption></figure>
## 4.2 Attitudes towards cheating: punishment vs reward

Figure 5 reports mean punishment rates by P2 SES × P1 SES × reported values. Punishment peaks at reports of 5 across pairings, with reports of 6 also attracting non-trivial punishment despite paying 0€. We relate to either a “larger number = more cheating” heuristic among some Observers, or to occasional misreadings of the payoff rules.

Conditioning on the same report, SES modulates severity more than scope. For instance, at 5, P2:High punish P1:Low/Med/High at comparable rates (0.194/0.258/0.254). The starkest asymmetry appears at 6, where P2:High are harsher toward P1:Low (0.312) relative to P2:Low→P1:Low (0.029) and P2:Med→P1:Low (0.161). On average, P2:Medium are the most punitive, while P2:Low the least. Importantly, same-SES cells (L-L, M-M, H-H) do not exhibit uniform leniency, as their rates at 5 cluster around one quarter, and at 6 range from very low (L-L) to mid-range (H-H). We also note that a few cells display zero observed punishment (e.g., P2:Low×P1:High at 1), which reflect small-N cells rather than missing data, therefore we annotate the figure so zero-height bars are visible rather than mistaken for missing observations. Appendix Table 10 reports, for every P2×P1×report cell, the counts and rates with exact confidence intervals.

<figure><img src="image_5.png" /><figcaption>Figure 5: Propensity to punish</figcaption></figure>

Figure 6 shows the mirror pattern for rewards. Across SES pairings, reward rates are generally high at reports 1-3 and drop at reports 5 and 6. For example, P2:Low reward P1:Low at 0.872, 0.912, and 0.957 for reports 1-3, and P2:High reward P1:Low at 0.857, 1.000, and 0.875 over the same range. By contrast, at report 5 several pairings exhibit the lowest rewards in their row, such as P2:Medium×P1:Medium at 0.464 and P2:High×P1:High at 0.461, while some pairings remain comparatively generous (e.g., P2:Low×P1:Low at 0.726). Report 6 is heterogeneous rather than uniformly low, with high rewards for
P2:Low×P1:High (0.857) but lower values for P2:High×P1:High (0.529) and P2:High×P1:Med (0.562).
Full counts and 95% CIs are in Appendix Table 11.

<figure><img src="image_6.png" /><figcaption>Figure 6: Propensity to reward</figcaption></figure>

# 5 Results

In this section we reports the results from our sample analyses. Unless stated otherwise, we estimate logistic regressions and report average marginal effects (AMEs) with cluster-robust standard errors by Observer (P2). Since each P2 makes 24 decisions, round-level observations are dependent, therefore, all models include round fixed effects to absorb common time patterns across the 24 rounds.

We address unobserved, stable differences across Observers in two ways. First, we estimate conditional logit models with Observer fixed effects, which use only within-Observer variation. Second, as a robustness check, we estimate linear probability models (LPM) with Observer fixed effects. These yield the same qualitative conclusions. For punishment (reward) regressions, we use rounds from the Punish (Reward) treatment and, from Mixed, only Observers assigned the corresponding condition. Observe-only rounds are excluded from enforcement regressions.

## 5.1 Decisions to punish across objective social distance

**Hypothesis 1.** Observers' propensity to punish increases when the counterpart is socially distant (vs. close).

The dependent variable is **punish**, equal to 1 when P2 applies a -2 penalty to P1's payoff in rounds where punishment is enabled (i.e., the Punish treatment; the punishment condition of the Mixed treat-
ment), and 0 otherwise. We use three regressors:

* **Suspicion of cheating:** *suspicious_report*, a round-level index that rises with unusually frequent payoff-maximising reports in the relevant Observer×SES exposure.

* **Objective social closeness:** *socially_close*, 1 if P1 and P2 reside in departments in the same SES tier, 0 otherwise.

* **Punishing close counterparts:** *suspicious_report_close*, interaction of previous variables, capturing whether responsiveness to the suspicion signal differs for socially close pairs.

The estimation sample pools all rounds from the Punish treatment and rounds from T3 (Mixed) for Observers assigned the Punish conditions.

Results show that punishment is responsive to the suspicion signal: (*suspicious_report* = 0.244, *p* < 0.010). Social closeness reduces this responsiveness: (*suspicious_report_close* = -0.164, *p* < 0.10), so the slope for socially close pairs is smaller ( 0.244 – 0.164 ≈ 0.08). Holding the signal fixed, socially close counterparts are punished less: (*socially_close* = -0.326, *p* < 0.05).

Disaggregating analyses by counterpart SES (Low as reference), distant pairs punish Medium and High more leniently than Low: (SES Medium = -0.352, *p* < 0.050) and (SES High = -0.424, *p* < 0.010). Social closeness offsets this pattern for High-SES counterparts (High#Socially close = 0.561, *p* < 0.01), while the Medium interaction is small and not significant (Medium#Socially close = 0.0887, *p* = 0.705).

Among controls, punishment is higher among women (+0.227, *p* < 0.050) and increases with age (+0.021 < 0.010); it is unrelated to occupation (+0.039, *p* = 0.171) and lower with education (-0.190, *p* < 0.010).

In sum, punishment rises with stronger suspicion, but this responsiveness is attenuated for socially close pairs. Conditional on the same suspicion level, Low-SES counterparts are more punished than Medium or High-SES ones. Although P1:High report 5s more often on average (Figure 3), Observers still sanction P1:Low more at a given suspicion level, consistent with socioeconomic selectivity in enforcement. The apparent leniency toward High-status counterparts is mostly a feature of distant pairings and disappears when counterparts are close.

Table 1 reports AMEs from the main logit with SEs clustered by Observer; robustness with two-way clustering (P2 and P1), Observer fixed effects (conditional logit), and LPM with Observer fixed effects yields qualitatively identical conclusions.

## 5.2 Decisions to punish across subjective social distance

We re-estimate the punishment model replacing objective closeness with the subjective measure. The dependent variable is *punish* (1 if P2 applies a –2 penalty in rounds where punishment is enabled; 0 otherwise). Key regressors:

* **Suspicion of cheating:** *suspicious_report*.

* **Subjective closeness:** *socially_close_subjective* =1 if P2's self-reported income tier matches P1's departmental tier; 0 otherwise.
<table><caption>Table 1: Punishment of socially close counterparts (objective)</caption><thead><tr><th>Variables</th><th>Punishment</th></tr></thead><tbody><tr><td>suspicious_report</td><td>0.244***<br>(0.058)</td></tr><tr><td>suspicious_report_close</td><td>-0.164*<br>(0.084)</td></tr><tr><td>SES Medium</td><td>-0.352**<br>(0.147)</td></tr><tr><td>SES High</td><td>-0.424***<br>(0.148)</td></tr><tr><td>socially_close</td><td>-0.326**<br>(0.150)</td></tr><tr><td>SES medium#Socially_close</td><td>0.088<br>(0.211)</td></tr><tr><td>SES high#Socially_close</td><td>0.561***<br>(0.210)</td></tr><tr><td>Gender (female = 1)</td><td>0.227**<br>(0.092)</td></tr><tr><td>Age</td><td>0.0210***<br>(0.004)</td></tr><tr><td>Occupation</td><td>0.039<br>(0.027)</td></tr><tr><td>Scholarship</td><td>-0.190***<br>(0.041)</td></tr><tr><td>Constant</td><td>0.603<br>(0.439)</td></tr><tr><td>Observations</td><td>3,456</td></tr></tbody></table>

Robust standard errors in parentheses. *p* < 0.10, **p* < 0.05, ***p* < 0.01.

• Suspicion × subjective closeness: suspicious_report_subj (interaction).

Controls include SES dummies for the counterpart (Medium, High; Low is the reference), their interactions with *socially_close_subj*, and controls. We estimate logit models, report average marginal effects (AMEs), use round fixed effects, and cluster standard errors by Observer (P2). Robustness checks with two-way clustering (P2&P1), conditional logit (P2 FE), and LPM with P2 FE yield similar conclusions.

Punishment responds positively to the suspicion signal (*suspicious_report* = 0.245, *p* < 0.010). Unlike the objective measure, moderation by subjective closeness is not significant (*suspicious_report_subj* = -0.127, *p* = 0.138), and there is no baseline difference by subjective closeness when holding the signal fixed (*socially_close_subj* = 0.168, *p* = 0.300).

By counterpart SES (vs. Low), punishment is lower for Medium and High (*SES Medium* = -0.357, *p* < 0.010; *SES High* = -0.329, *p* < 0.05). Interactions with subjective closeness are not significant for Medium (+0.236, *p* = 0.325) and only marginal for High-SES (+0.434, *p* < 0.10). Moreover, punishment is higher among women (+0.287, *p* < 0.010) and with age (+0.020, *p* < 0.010), weakly higher with occupation (+0.0495, *p* < 0.100), and lower with education (-0.202, *p* < 0.010).

Consistent with H1, punishment increases with the suspicion index. However, using the subjective closeness measure we do not detect a reliable distance effect (neither a main effect of closeness nor a stable attenuation of the suspicion–punishment slope). The SES pattern persists: at comparable suspicion, Medium and High-SES counterparts are punished less than Low-SES counterparts, with only a
<table><caption>Table 2: Punishment of socially close counterparts (subjective)</caption><thead><tr><th>Variables</th><th>Punishment</th></tr></thead><tbody><tr><td>suspicious_report</td><td>0.245***<br>(0.054)</td></tr><tr><td>suspicious_report_subjective</td><td>-0.127<br>(0.085)</td></tr><tr><td>SES Medium</td><td>-0.357***<br>(0.135)</td></tr><tr><td>SES High</td><td>-0.329**<br>(0.141)</td></tr><tr><td>Socially close subjective</td><td>0.168<br>(0.162)</td></tr><tr><td>SES Medium#Socially close subjective</td><td>0.236<br>(0.240)</td></tr><tr><td>SES High#Socially close subjective</td><td>0.434*<br>(0.233)</td></tr><tr><td>Gender (female = 1)</td><td>0.287***<br>(0.096)</td></tr><tr><td>Age</td><td>0.020***<br>(0.004)</td></tr><tr><td>Occupation</td><td>0.0495*<br>(0.029)</td></tr><tr><td>Scholarship</td><td>-0.202***<br>(0.042)</td></tr><tr><td>Constant</td><td>0.38<br>(0.440)</td></tr><tr><td>Observations</td><td>3,456</td></tr></tbody></table>

Robust standard errors in parentheses *p* < 0.10, **p* < 0.05, ***p* < 0.01.

marginal uptick when High-SES targets are subjectively close. Overall, these results support the evidence- responsiveness component of H1 but do not provide clear support for a subjective-closeness moderation. See Table 2) for full estimates (AMEs), clustered SEs by P2, and listed robustness checks.

## 5.3 Decisions to reward across objective social distance

**Hypothesis 2.** Observers' propensity to reward increases when the counterpart is socially close.

The dependent variable is *reward* (1 if P2 adds +2 to P1's payoff in reward-enabled rounds; 0 otherwise). We estimate a logit and report average marginal effects with standard errors clustered by Observer (P2); round fixed effects are included. The estimating sample pools the Reward treatment and, from Mixed, only Observers assigned reward conditions (Observe-only rounds excluded). We use three key regressors:

* Suspicion of cheating: *suspicion gain*.

* Objective social closeness: *socially close* P1 and P2 in the same SES tier.

* Moderation: *suspicion gain close* = *suspicion gain* × *socially close*.

And add *ses* tier dummies for P1 (reference: Low-SES), their interactions with *socially close*, and demographic controls.

Rewards move inversely with the suspicion index (*suspicion gain* = -0.241, *p* < 0.010), indicating more rewards when reports look non-suspicious. Objective closeness does not change this responsiveness
(suspicion gain close = 0.008, p = 0.908). Holding suspicion fixed, socially close counterparts receive more rewards (socially close = 0.578, p < 0.010).

By counterpart SES, main effects are small and not significant (Medium = -0.106, p = 0.409; High = 0.193, p = 0.147), but closeness effects attenuate with status: Medium × Close = -0.531, p < 0.01; High × Close = -0.977, p < 0.01. Moreover, women reward less (-0.166, p < 0.050), while age and occupation are not significant (-0.003, p = 0.415; -0.027, p = 0.237); education is positively associated with rewarding (0.092, p < 0.010).

In sum, results show that rewards are higher when suspicious cues are weaker. However, closeness does not alter sensitivity to the suspicion signal, but it does shape who benefits at a given level of suspicion: close, low-SES counterparts are favoured, the advantage fades for Medium and reverses for High-SES. Robustness (two-way clustering by P1 and P2; conditional logit with Observer FE; LPM with Observer FE) yields the same significant conclusions.

<table><caption>Table 3: Rewards of socially close counterparts (objective)</caption><thead><tr><th>Variables</th><th>Reward</th></tr></thead><tbody><tr><td>suspicious_report</td><td>-0.241***<br>(0.051)</td></tr><tr><td>suspicious_report_close</td><td>0.0084<br>(0.073)</td></tr><tr><td>SES Medium</td><td>-0.106<br>(0.129)</td></tr><tr><td>SES High</td><td>0.193<br>(0.133)</td></tr><tr><td>Social closeness</td><td>0.578***<br>(0.141)</td></tr><tr><td>SES Medium#Socially close</td><td>-0.531***<br>(0.187)</td></tr><tr><td>SES High#Social closeness</td><td>-0.977***<br>(0.188)</td></tr><tr><td>Gender (female = 1)</td><td>-0.166**<br>(0.080)</td></tr><tr><td>Age</td><td>-0.003<br>(0.003)</td></tr><tr><td>Occupation</td><td>-0.027<br>(0.023)</td></tr><tr><td>Scholarship</td><td>0.092***<br>(0.033)</td></tr><tr><td>Constant</td><td>0.535<br>(0.385)</td></tr><tr><td>Observations</td><td>3,456</td></tr></tbody></table>

Robust standard errors in parentheses; *p* < 0.10, **p* < 0.05, ***p* < 0.01.

## 5.4 Decisions to reward across subjective social distance

We re-estimate the reward model replacing objective closeness with the subjective measure. The dependent variable is *reward* (1 if P2 adds +2 in reward-enabled rounds; 0 otherwise). We estimate a logit and report average marginal effects (AMEs) with standard errors clustered by P2. We use the following key regressors:

* Suspicion of cheating: suspicion gain.
* **Subjective social closeness:** *socially_close_subjective* (P2's subjective SES matches P1's departmental SES tier).

* **Moderation:** *suspicion gain subjective* = *suspicion gain* × *socially close subjective*.

Rewards move inversely with the suspicion index (*suspicion gain* = -0.313, *p* < 0.01), indicating more rewards when reports look non-suspicious. Unlike the objective specification, subjective closeness does moderate this responsiveness: *suspicion gain subjective* = 0.210 (*p* < 0.010). Given the negative baseline slope, this implies a substantially weaker decline in rewarding as suspicion rises for subjectively close pairs (about -0.313+0.210 ≈ -0.103). Holding other regressors fixed, there is no baseline difference by subjective closeness (*socially_close_subjective* = -0.088, *p* = 0.575).

By counterpart SES, rewards are lower for P1:High (Medium = -0.460, *p* < 0.010; High = -0.393, *p* < 0.010). Subjective closeness partly offsets this for P1:Medium (Medium×Close = 0.385, *p* = 0.070) and P1:High (High×Close = 0.438, *p* = 0.060), both with marginal numbers. Among controls, education is positively associated with rewarding (0.075, *p* < 0.050), while gender, age and occupation are not significant at conventional levels.

Consistent with H2's evidence channel, Observers reward less as suspicious cues grow stronger. Under the *subjective closeness* measure, this sensitivity is attenuated for subjectively close pairs: when P2 feels close to P1, the decline in rewarding with rising suspicion is smaller. Baseline rewarding does not differ by subjective closeness at a given suspicion level. Status patterns persist—Medium- and High-SES Rollers are rewarded less than Low-SES at comparable suspicion—though subjective closeness marginally tempers this gap.

Rewards move inversely with the suspicion index: observers are more likely to reward when reports appear non-suspicious. Unlike the objective measure, subjective closeness moderates responsiveness, as the decrease in rewards when suspicions of cheating rise is weaker for subjectively close pairs. Moreover, there is no baseline difference between subjectively close and distant counterparts at a given suspicion level. By counterpart SES, rewards are lower for medium and high-SES than for low-SES at comparable suspicion levels, while subjective closeness partly offsets this for medium and high status but only marginally. In short, under the subjective measure of closeness, as suspicion of cheating goes up, most Observers reward less. But when they feel subjectively close to the person, that drop in rewarding is smaller.
<table><caption>Table 4: Rewards of socially close counterparts (subjective)</caption><thead><tr><th>Variables</th><th>Reward</th></tr></thead><tbody><tr><td>suspicious_report</td><td>-0.313***<br>(0.044)</td></tr><tr><td>suspicious_report_subjective</td><td>0.210***<br>(0.079)</td></tr><tr><td>SES Medium</td><td>-0.460***<br>(0.118)</td></tr><tr><td>SES High</td><td>-0.393***<br>(0.117)</td></tr><tr><td>Socially close subjective</td><td>-0.088<br>(0.158)</td></tr><tr><td>SES Medium#Socially close subjective</td><td>0.385*<br>(0.213)</td></tr><tr><td>SES High#Socially close subjective</td><td>0.438*<br>(0.233)</td></tr><tr><td>Gender (female = 1)</td><td>-0.112<br>(0.081)</td></tr><tr><td>Age</td><td>-0.003<br>(0.004)</td></tr><tr><td>Occupation</td><td>-0.002<br>(0.024)</td></tr><tr><td>Scholarity</td><td>0.075**<br>(0.034)</td></tr><tr><td>Constant</td><td>0.663*<br>(0.395)</td></tr><tr><td>Observations</td><td>3,456</td></tr></tbody></table>

Robust standard errors in parentheses; *p < 0.10, **p < 0.05, ***p < 0.01.

# 6 Concluding Remarks

This paper investigated whether third-party norm enforcement in a Die-under-the-Cup setting is associated with social closeness and socioeconomic status. Across four regressions that introduced decisions to punish and reward, each with an objective and a subjective measure of closeness, the main result is clear: enforcement is predominantly driven by suspicions of cheating and asymmetrically associated with socioeconomic status. Our findings show that decisions to punish increase in parallel to suspicions of cheating, while decision to reward increase as these same suspicions weaken.

A key component of our study is the proposed proxy to capture suspicious reports in the DUTC, as this allowed us to estimate responses that faithfully depict norm enforcement. The fact that punishment rises and reward falls along with the index across specifications supports the proxy's construct validity and portability to other private-report contexts, especially when anonymity needs to be preserved in order to obtain more reliable answers.

As for the selectiveness of norm enforcement, our results provide a clear picture of how social closeness shapes the baseline level of sanctions and, in some cases, how sensitive those sanctions are to the suspicion signal. Under our objective measure of closeness, close counterparts are punished less than distant ones at the same suspicion level. For rewards, close pairs have a higher baseline likelihood of being rewarded at a given suspicion. This baseline difference is largest for low-SES counterparts, small for medium-SES, and reverses for high-SES. Moreover, the reward-suspicion slope does not change with objective closeness, so the difference comes from levels rather than responsiveness. Under subjective closeness, punishment levels
and slopes remain tied to the signal with no reliable changes, while rewards show reduced sensitivity to suspicion: as suspicion rises, rewards decline more slowly for subjectively close pairs, without a systematic lift or drop in baseline levels. Our results not only illustrate the way in which capturing closeness from different angles can shift norm enforcement, but also that a simple mechanism such as living in the same area can induce feelings of closeness.

On the other hand, socioeconomic status interacts with these patterns in a systematic way. One of the most telling results is that socioeconomic status interacts with these patterns to punish low-SES counterparts more than higher SES ones for the same suspicion signal, echoing previous studies suggesting that socioeconomic bias is negatively skewed against lower-income individuals. At the same time, closeness to high-status counterparts removes much of the leniency observed elsewhere, implying that the more punitive observers to high-income participants are other high-income individuals. This signal higher standards among high SES participants, reducing the gap in treatment. On the reward side, the asymmetry is complementary: under objective closeness, extra rewards concentrate on low-status counterparts, are small for medium-status, and turn negative for high-status. Under subjective closeness, the baseline premium fades, but closeness softens the decline in rewards as suspicion grows, indicating a closeness-based tolerance to ambiguous signals rather than a general lift in generosity.

Overall, our findings speak to the literature on selective norm enforcement and status expectations. They show that behaviour drives sanctions, with distance and status selectively tilting how strongly observability is converted into action. They also clarify why studies alternately find distance-based asymmetries or null effects: objective, place-based closeness shifts baselines and interacts with status; subjective, *post hoc* similarity softens the link between evidence and generosity without moving baselines.

**Limitations and future directions** There are two caveats that frame interpretation in our analyses. First, while the socioeconomic status is consistent with expectation-based standards, isolating mechanisms such as inequality aversion or deservingness would require a design that orthogonally vary inequality transparency and attribution cues to further infer the impact of SES differences. Second, while modelling socioeconomic closeness at the department level proves a reliable measure, it may blur heterogeneity within large or unequal areas in more fine-grained analyses. Finer geographic income data could sharpen identification. Future work should (1) test other distance dimensions (friendship, politics, ethnicity, workplace), (2) examine contexts where Observers bear costs or face accountability for sanctions, (3) and replicate in field or organisational settings with richer administrative data.

**Policy implications** There are two leading implications for practical implementation of our analyses. First, decisions are evidence-driven: rewards rise when suspicion is low and punishments rise when suspicion is high. Second, enforcement is socially selective: leniency for close others and harsher sanctions for low-status counterparts at comparable evidence levels. Organisations can act on both: make evidence the focal point (clear thresholds, structured checklists), and reduce identity-based skew (mask socio-economic cues where possible; separate evidence review from identity; use blind panels). Reward mechanisms that recognise clear “non-suspicion” can strengthen compliance without stigmatising low-status groups; conversely, sanction policies should be audited for SES-linked disparities and calibrated with transparent guidelines.
**Contribution and originality.** We recast third-party enforcement as an evidence-to-action process and show how social closeness shapes that conversion. Methodologically, we build a continuous suspicion index anchored in chance and incentives, using only what each observer actually sees. This observer-level, payoff-aligned signal preserves the DUTC's core logic while moving beyond population averages to the decision environment each observer faced. Our design is stake-free and two-sided: the same informational signal applies to both, punishment and reward enforcement, allowing clean comparisons of how identical evidence translates into sanctions versus bonuses.

Substantively, the structure lets us separate who the target is from how evidence is used. Moreover, by manipulating closeness with two measures, we can provide inferences on how objective closeness mainly shifts levels of enforcement, tilting the average treatment people receive, while subjective closeness mainly shifts responsiveness, altering how sharply observers react to the same evidence.

Furthermore, conditioning on the suspicion index makes status-linked selectivity salient to observe how socioeconomic differences change approaches to enforcement. These patterns refine accounts of in-group favouritism by showing that proximity does not replace evidence, but it biases the conversion of the same evidence into action.

Furthermore, the suspicion index is computed only from the distribution of registered values that an Observer sees and the payoff mapping, so it can be applied wherever truthful answers or reporting is hidden by design. Because punishment and reward are both responses to the same signal and carry no stakes for Observers, we obtain a unified measurement of enforcement that is directly comparable across levers
# 7 Appendix

<table><caption>Table 5: Demographics on scholarship</caption><thead><tr><th>Diploma</th><th>Observations</th><th>Participants</th></tr></thead><tbody><tr><td>PhD (8+ years)</td><td>1,104</td><td>46</td></tr><tr><td>Master (5 years)</td><td>8,664</td><td>361</td></tr><tr><td>Bachelor (3-4 years)</td><td>4,248</td><td>177</td></tr><tr><td>Technical degree (2 years)</td><td>1,440</td><td>60</td></tr><tr><td>High school diploma</td><td>1,536</td><td>64</td></tr><tr><td>Secondary education</td><td>192</td><td>8</td></tr><tr><td>No diploma</td><td>96</td><td>4</td></tr><tr><td>Total</td><td>17,280</td><td>720</td></tr></tbody></table>

<table><caption>Table 6: Demographics on occupation</caption><thead><tr><th>Occupation</th><th>Observations</th><th>Participants</th></tr></thead><tbody><tr><td>Employed (manager or independent)</td><td>2,928</td><td>122</td></tr><tr><td>Employed</td><td>3,840</td><td>160</td></tr><tr><td>Independent</td><td>936</td><td>39</td></tr><tr><td>Pensioner</td><td>312</td><td>13</td></tr><tr><td>Unemployed</td><td>1,704</td><td>71</td></tr><tr><td>Student</td><td>7,128</td><td>297</td></tr><tr><td>Working students</td><td>3,768</td><td>157</td></tr><tr><td>Other</td><td>432</td><td>18</td></tr><tr><td>Total</td><td>17,280</td><td>720</td></tr></tbody></table>

<table><caption>Table 7: Distribution of die-roll reports by Die-rollers (P1)</caption><thead><tr><th>Roll value</th><th>Observations</th><th>Observed %</th><th>Expectation</th><th>Δ</th></tr></thead><tbody><tr><td>1</td><td>1,204</td><td>13.9%</td><td>≈ 16.7%</td><td>-2.8</td></tr><tr><td>2</td><td>1,222</td><td>14.1%</td><td>≈ 16.7%</td><td>-2.6</td></tr><tr><td>3</td><td>1,420</td><td>16.4%</td><td>≈ 16.7%</td><td>-0.3</td></tr><tr><td>4</td><td>1,367</td><td>15.8%</td><td>≈ 16.7%</td><td>-0.9</td></tr><tr><td>5</td><td>2,286</td><td>26.5%</td><td>≈ 16.7%</td><td>+9.8</td></tr><tr><td>6</td><td>1,141</td><td>13.2%</td><td>≈ 16.7%</td><td>-3.5</td></tr></tbody></table>

16.7% is the expected uniform distribution for each reported die-roll; Δ is the difference from each aggregate reported outcome to the expected value in percentage.
<table><caption>Table 8: Distribution of die-roll reports by Observers (P2)</caption><thead><tr><th>Roll value</th><th>Observations</th><th>Observed %</th><th>Expectation</th><th>Δ</th></tr></thead><tbody><tr><td>1</td><td>725</td><td>8.39%</td><td>≈ 16.7%</td><td>-8.31</td></tr><tr><td>2</td><td>993</td><td>11.49%</td><td>≈ 16.7%</td><td>-5.21</td></tr><tr><td>3</td><td>1,306</td><td>15.12%</td><td>≈ 16.7%</td><td>-1.58</td></tr><tr><td>4</td><td>1,434</td><td>16.60%</td><td>≈ 16.7%</td><td>-0.10</td></tr><tr><td>5</td><td>3,371</td><td>39.02%</td><td>≈ 16.7%</td><td>+22.32</td></tr><tr><td>6</td><td>811</td><td>9.39%</td><td>≈ 16.7%</td><td>-7.31</td></tr></tbody></table>

<table><caption>Table 9: Departments of residence in the sample (by observations)</caption><thead><tr><th>Department</th><th>Observations</th><th>Percentage (%)</th></tr></thead><tbody><tr><td>Bas-Rhin</td><td>1,656</td><td>9.58</td></tr><tr><td>Bouches-du-Rhône</td><td>264</td><td>1.53</td></tr><tr><td>Essonne</td><td>552</td><td>3.19</td></tr><tr><td>Haut-Rhin</td><td>192</td><td>1.11</td></tr><tr><td>Hauts-de-Seine</td><td>1,656</td><td>9.58</td></tr><tr><td>Maine-et-Loire</td><td>120</td><td>0.69</td></tr><tr><td>Meurthe-et-Moselle</td><td>240</td><td>1.39</td></tr><tr><td>Moselle</td><td>600</td><td>3.47</td></tr><tr><td>Nord</td><td>432</td><td>2.50</td></tr><tr><td>Paris</td><td>4,104</td><td>23.76</td></tr><tr><td>Pas-de-Calais</td><td>192</td><td>1.11</td></tr><tr><td>Rhône</td><td>144</td><td>0.83</td></tr><tr><td>Seine-Maritime</td><td>552</td><td>3.19</td></tr><tr><td>Seine-Saint-Denis</td><td>1,968</td><td>11.39</td></tr><tr><td>Seine-et-Marne</td><td>312</td><td>1.81</td></tr><tr><td>Val-d'Oise</td><td>504</td><td>2.92</td></tr><tr><td>Val-de-Marne</td><td>648</td><td>3.75</td></tr><tr><td>Yvelines</td><td>384</td><td>2.22</td></tr><tr><td>Other</td><td>2,760</td><td>15.97</td></tr></tbody><tfoot><tr><td><strong>Total</strong></td><td>17,280</td><td>100.00</td></tr></tfoot></table>

Only departments with more than 100 observations (i.e., at least 5 participants) are shown in the table. The rest are compiled under "Other".
<table><caption>Table 10: Punishment by P2 SES × P1 SES and reported value: rate [95% CI]</caption><thead><tr><th>P2-P1 pairing</th><th>Report 1</th><th>Report 2</th><th>Report 3</th></tr></thead><tbody><tr><td>P2 Low - P1 Low</td><td>0.103 [0.029, 0.242] (39)</td><td>0.222 [0.120, 0.356] (54)</td><td>0.171 [0.072, 0.321] (41)</td></tr><tr><td>P2 Low - P1 Med</td><td>0.231 [0.050, 0.538] (13)</td><td>0.316 [0.126, 0.566] (19)</td><td>0.278 [0.142, 0.452] (36)</td></tr><tr><td>P2 Low - P1 High</td><td>0.000 [0.000, 0.308] (10)</td><td>0.050 [0.001, 0.249] (20)</td><td>0.050 [0.001, 0.249] (20)</td></tr><tr><td>P2 Med - P1 Low</td><td>0.250 [0.087, 0.491] (20)</td><td>0.095 [0.012, 0.304] (21)</td><td>0.000 [0.000, 0.161] (21)</td></tr><tr><td>P2 Med - P1 Med</td><td>0.262 [0.139, 0.420] (42)</td><td>0.116 [0.039, 0.251] (43)</td><td>0.216 [0.098, 0.382] (37)</td></tr><tr><td>P2 Med - P1 High</td><td>0.333 [0.099, 0.651] (12)</td><td>0.200 [0.043, 0.481] (15)</td><td>0.238 [0.082, 0.472] (21)</td></tr><tr><td>P2 High - P1 Low</td><td>0.000 [0.000, 0.195] (17)</td><td>0.100 [0.012, 0.317] (20)</td><td>0.172 [0.058, 0.358] (29)</td></tr><tr><td>P2 High - P1 Med</td><td>0.130 [0.028, 0.336] (23)</td><td>0.083 [0.010, 0.270] (24)</td><td>0.125 [0.016, 0.383] (16)</td></tr><tr><td>P2 High - P1 High</td><td>0.250 [0.107, 0.449] (28)</td><td>0.162 [0.062, 0.320] (37)</td><td>0.083 [0.018, 0.225] (36)</td></tr></tbody><thead><tr><th>P2-P1 pairing</th><th>Report 4</th><th>Report 5</th><th>Report 6</th></tr></thead><tbody><tr><td>P2 Low - P1 Low</td><td>0.167 [0.075, 0.302] (48)</td><td>0.250 [0.155, 0.366] (72)</td><td>0.029 [0.001, 0.153] (34)</td></tr><tr><td>P2 Low - P1 Med</td><td>0.250 [0.107, 0.449] (28)</td><td>0.371 [0.215, 0.551] (35)</td><td>0.154 [0.019, 0.454] (13)</td></tr><tr><td>P2 Low - P1 High</td><td>0.150 [0.032, 0.379] (20)</td><td>0.286 [0.173, 0.422] (56)</td><td>0.111 [0.014, 0.347] (18)</td></tr><tr><td>P2 Med - P1 Low</td><td>0.083 [0.010, 0.270] (24)</td><td>0.111 [0.024, 0.292] (27)</td><td>0.161 [0.055, 0.337] (31)</td></tr><tr><td>P2 Med - P1 Med</td><td>0.094 [0.031, 0.207] (53)</td><td>0.269 [0.175, 0.382] (78)</td><td>0.200 [0.084, 0.369] (35)</td></tr><tr><td>P2 Med - P1 High</td><td>0.286 [0.113, 0.522] (21)</td><td>0.375 [0.249, 0.515] (56)</td><td>0.158 [0.034, 0.396] (19)</td></tr><tr><td>P2 High - P1 Low</td><td>0.077 [0.009, 0.251] (26)</td><td>0.194 [0.082, 0.360] (36)</td><td>0.312 [0.110, 0.587] (16)</td></tr><tr><td>P2 High - P1 Med</td><td>0.250 [0.098, 0.467] (24)</td><td>0.258 [0.119, 0.446] (31)</td><td>0.038 [0.001, 0.196] (26)</td></tr><tr><td>P2 High - P1 High</td><td>0.206 [0.087, 0.379] (34)</td><td>0.254 [0.177, 0.344] (114)</td><td>0.256 [0.130, 0.421] (39)</td></tr></tbody></table>

Notes: Each entry is the mean punishment rate with exact (Clopper-Pearson) 95% confidence interval and cell size *N*. Example: 0.103 [0.029, 0.242] (39) means a 10.3% punishment rate, 95% CI 2.9%–24.2%, from *N* = 39 observations.

<table><caption>Table 11: Reward by P2 SES × P1 SES and reported value: rate [95% CI]</caption><thead><tr><th>P2-P1 pairing</th><th>Report 1</th><th>Report 2</th><th>Report 3</th></tr></thead><tbody><tr><td>P2 Low - P1 Low</td><td>0.872 [0.726, 0.957] (39)</td><td>0.912 [0.763, 0.981] (34)</td><td>0.957 [0.852, 0.995] (46)</td></tr><tr><td>P2 Low - P1 Med</td><td>0.850 [0.621, 0.968] (20)</td><td>0.750 [0.476, 0.927] (16)</td><td>0.793 [0.603, 0.920] (29)</td></tr><tr><td>P2 Low - P1 High</td><td>0.950 [0.751, 0.999] (20)</td><td>0.762 [0.528, 0.918] (21)</td><td>0.767 [0.577, 0.901] (30)</td></tr><tr><td>P2 Med - P1 Low</td><td>0.909 [0.708, 0.989] (22)</td><td>0.920 [0.740, 0.990] (25)</td><td>0.636 [0.407, 0.828] (22)</td></tr><tr><td>P2 Med - P1 Med</td><td>0.828 [0.642, 0.942] (29)</td><td>0.837 [0.703, 0.927] (49)</td><td>0.757 [0.588, 0.882] (37)</td></tr><tr><td>P2 Med - P1 High</td><td>0.857 [0.673, 0.960] (28)</td><td>0.812 [0.544, 0.960] (16)</td><td>0.765 [0.501, 0.932] (17)</td></tr><tr><td>P2 High - P1 Low</td><td>0.857 [0.572, 0.982] (14)</td><td>1.000 [0.858, 1.000] (24)</td><td>0.875 [0.676, 0.973] (24)</td></tr><tr><td>P2 High - P1 Med</td><td>0.778 [0.524, 0.936] (18)</td><td>0.714 [0.419, 0.916] (14)</td><td>0.588 [0.329, 0.816] (17)</td></tr><tr><td>P2 High - P1 High</td><td>0.706 [0.525, 0.849] (34)</td><td>0.812 [0.636, 0.928] (32)</td><td>0.756 [0.597, 0.876] (41)</td></tr></tbody><thead><tr><th>P2-P1 pairing</th><th>Report 4</th><th>Report 5</th><th>Report 6</th></tr></thead><tbody><tr><td>P2 Low - P1 Low</td><td>0.647 [0.501, 0.776] (51)</td><td>0.726 [0.609, 0.824] (73)</td><td>0.689 [0.534, 0.818] (45)</td></tr><tr><td>P2 Low - P1 Med</td><td>0.714 [0.478, 0.887] (21)</td><td>0.550 [0.385, 0.707] (40)</td><td>0.444 [0.215, 0.692] (18)</td></tr><tr><td>P2 Low - P1 High</td><td>0.714 [0.537, 0.854] (35)</td><td>0.667 [0.447, 0.844] (24)</td><td>0.857 [0.572, 0.982] (14)</td></tr><tr><td>P2 Med - P1 Low</td><td>0.680 [0.465, 0.851] (25)</td><td>0.538 [0.334, 0.734] (26)</td><td>0.750 [0.533, 0.902] (24)</td></tr><tr><td>P2 Med - P1 Med</td><td>0.652 [0.498, 0.786] (46)</td><td>0.464 [0.355, 0.576] (84)</td><td>0.698 [0.539, 0.828] (43)</td></tr><tr><td>P2 Med - P1 High</td><td>0.684 [0.434, 0.874] (19)</td><td>0.654 [0.509, 0.780] (52)</td><td>0.667 [0.349, 0.901] (12)</td></tr><tr><td>P2 High - P1 Low</td><td>0.792 [0.578, 0.929] (24)</td><td>0.622 [0.448, 0.775] (37)</td><td>0.619 [0.384, 0.819] (21)</td></tr><tr><td>P2 High - P1 Med</td><td>0.542 [0.328, 0.744] (24)</td><td>0.513 [0.348, 0.676] (39)</td><td>0.562 [0.377, 0.736] (32)</td></tr><tr><td>P2 High - P1 High</td><td>0.655 [0.519, 0.775] (58)</td><td>0.461 [0.354, 0.570] (89)</td><td>0.529 [0.351, 0.702] (34)</td></tr></tbody></table>

Notes: Each entry is the mean reward rate with exact (Clopper-Pearson) 95% confidence interval and cell size *N*.
<figure><img src="image_7.png" /><figcaption>Figure 7: Participants’ departments of residence by SES</figcaption></figure>

The map shows the departments where participants registered for the experiment by SES level:

**Low-income:** Aisne, Aveyron, Bouches-du-Rhone, Calvados, Charente-Maritime, Cher, Cotes-d'Armor, Deux-Sèvres, Drome, Eure-et-Loir, Haute-Loire, Haute-Saône, Haute-Savoie, Hérault, Indre, Isère, Loir-et-Cher, Loire, Maine-et-Loire, Manche, Marne, Meurthe-et-Moselle, Moselle, Nord, Pas-de-Calais, Pyrénées-Orientales, Saône-et-Loire, Seine-Maritime, Seine-Saint-Denis, Somme, Tarn, Tarn-et-Garonne, Territoire de Belfort, Vaucluse, Vendée, Vienne.

**Medium-income:** Ain, Alpes-Maritimes, Bas-Rhin, Doubs, Essonne, Finistère, Gironde, Haut-Rhin, Haute-Garonne, Indre-et-Loire, Loire-Atlantique, Morbihan, Oise, Puy-de-Dôme, Pyrénées-Atlantiques, Rhône, Savoie, Seine-et-Marne, Val-d'Oise, Val-de-Marne, Var, Yvelines, Ille-et-Vilaine.

**High-income:** Hauts-de-Seine, Paris.
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