Dictator Game

What it is

In the dictator game, one player receives a fixed endowment and decides how much to keep and how much to transfer to a second player. The recipient cannot refuse or retaliate; they simply receive whatever the dictator allocates. This one-sided structure removes strategic incentives: there is no reason to give based on reciprocity, reputation, or fear of punishment. Whatever the dictator transfers reflects their preferences about the distribution of payoffs between themselves and another person.

The paradigm was introduced by Kahneman, Knetsch & Thaler (1986) as a fairness test embedded in an economics-class survey; Forsythe, Horowitz, Savin & Sefton (1994) ran the first formal incentivised side-by-side comparison with the ultimatum game and is the canonical reference for the incentivised version. Engel’s (2011) meta-analysis of 129 papers and 328 treatments finds dictators give an average of 28% of the endowment, with substantial bimodality — large masses at zero and at the equal split — and a small but detectable negative stake effect.

When to use it

The dictator game is appropriate as a baseline measure of pro-social preferences — generosity, altruism, distributional concern — in contexts where strategic confounds would obscure the signal. It is most often paired with the trust game and the ultimatum game: the dictator game provides the non-strategic baseline; the trust game adds reciprocity; the ultimatum game adds punishment by the recipient.

For settings where survey time is tight or behavioural-experiment infrastructure is unavailable, the Global Preference Survey altruism module (Falk, Becker, Dohmen, Enke, Huffman & Sunde, 2018) is a five-minute survey-based alternative that correlates with incentivised dictator transfers across 76 countries. Use the survey module when the constraint is time or operational complexity; use an incentivised dictator game when the comparison is across treatments or arms where session-controlled incentives matter.

Cross-cultural and field uses are well established: Henrich, Boyd, Bowles, Camerer, Fehr, Gintis & McElreath (2005) reported dictator and ultimatum results from 15 small-scale societies, establishing substantial cross-cultural variation; Ensminger & Henrich (2014) extended this with a comparison-site design that included urban industrial samples. In development field research, the dictator game has been used to measure social cohesion within communities, to compare pro-social preferences across social groups, and to test whether a programme shifts distributional preferences.

The dictator game is less appropriate when the construct of interest is itself strategic — reciprocity (use the trust game), punishment (use the ultimatum game), or sanctioning in public-goods provision (use the public goods game with punishment).

How it works

The standard implementation has three steps:

Step 1 — Role assignment and pairing. Random assignment to dictator and recipient roles, and random pairing of dictators with recipients. Field implementations commonly use unilateral pairing: a single live respondent decides an allocation that will be paid to an absent or unidentified partner — another respondent from a separate session, a respondent from a different village, or a known charity. The recipient pool changes what the game measures and is a Key decision below.

Step 2 — Allocation decision. The dictator is given an endowment (cash directly, or tokens later exchanged at a fixed rate) and decides how to split it between themselves and the recipient. The show-up fee must be paid and visibly framed as unconditional and separate from the endowment — pooling them depresses giving because dictators treat the combined sum as quasi-earned compensation.

Step 3 — Payment. Both parties are paid according to the dictator’s decision. Under double-blind anonymity protocols, payment is arranged so that neither the recipient nor the experimenter can link choices to individuals (Hoffman, McCabe & Smith, 1996).

The primary outcome is the transfer share — amount sent divided by the endowment. Standard descriptive outputs are the mean, the focal-point masses at 0 and 0.5, and the bimodality diagnostic.

Identification assumptions. A dictator transfer is interpretable as a distributional preference only under:

1. Belief in consequentiality. The dictator believes the recipient is real and the payment will be made. Field implementations often add a worked example with a third respondent visibly receiving payment from a prior session to demonstrate consequentiality.
2. Anonymity from the recipient and, ideally, the experimenter. Hoffman, McCabe & Smith (1996) show that giving drops sharply when the recipient cannot identify the dictator and the experimenter cannot identify individual choices.
3. Frame neutrality. The choice set and language are not themselves a treatment — no “take” option unless the take-versus-give variation is the research question (List, 2007; Bardsley, 2008), no priming words like “share,” “donate,” or “charity” unless the priming is the treatment (Branas-Garza, 2007).
4. Comprehension. The dictator understands that they can keep any non-negative amount up to the full endowment, that the recipient cannot refuse, and that the payment is real. Pre-decision comprehension checks are required in low-literacy contexts.
5. Endowment is windfall, not earned. Cherry, Frykblom & Shogren (2002) showed that when dictators earn the endowment through a real-effort task, average giving collapses to near zero — the standard “windfall endowment” implementation is what the 28% benchmark applies to.

Key decisions

Anonymity. Hoffman, McCabe & Smith (1996) show that double-blind anonymity — where the experimenter as well as the recipient cannot identify the dictator — reduces average giving by roughly half compared to single-blind. In field settings, true double-blind is operationally costly; document the protocol explicitly (who can see the allocation? when is the payment made? is the dictator’s choice visible on the enumerator’s tablet?).

Endowment origin: windfall vs. earned. Cherry, Frykblom & Shogren (2002) is the single most important robustness finding on DG — earning the endowment through real effort collapses giving toward zero. If the research question concerns “real” altruism rather than the windfall benchmark, use an earned endowment; if comparison with the 28% literature is needed, use a windfall endowment. State the choice and its rationale.

Stake size. Engel’s (2011) meta-analysis finds a small but statistically detectable negative effect of stakes on transfer share — higher stakes, slightly lower share — but the rank order of treatment effects across studies is stable. Stakes should be meaningful relative to local daily income but not so large as to create wealth effects that distort subsequent games in a battery.

Recipient pool. The recipient identity is a first-order design choice that the standard treatment of DG obscures: (i) another respondent from the same village; (ii) another respondent from a different village; (iii) a known charity; (iv) the enumerator (rare and contaminating — never recommended); (v) a hypothetical anonymous stranger. Each measures a different construct (Charness & Gneezy, 2008). Document the choice and avoid (iv) in field settings.

In-group vs. out-group recipients. Dictators give substantially more to community members, co-ethnics, or known recipients than to strangers. The in-group premium is much larger when recipient identity is given by category labels (caste, ethnicity, religion) than when recipients are personally known. Randomise recipient type to identify the premium directly; cluster SEs at the dictator level when each dictator decides over multiple recipient types.

Strategy method vs. direct response. The strategy method asks the dictator to choose conditional on each possible recipient identity (“if you were paired with X, how much would you send?”). It provides richer data per participant but increases the cognitive load and may make the hypothetical structure salient. Brandts & Charness (2011) review the evidence on strategy-vs-direct comparisons and find that the two methods produce qualitatively similar results in DG, with some quantitative differences in level.

Give-only vs. give-or-take. The standard frame is give-only — the dictator starts with the full endowment and can transfer none, some, or all of it. List (2007) and Bardsley (2008) added the take option (both players start with an endowment, the dictator can give or take) and showed that giving in the standard frame is partly an artefact of the action space: when taking is available, net transfers fall sharply. If the research question is “pure altruism,” the give-or-take frame is the more honest benchmark.

Comprehension and order in a battery. When DG is part of a battery, randomise the game order and either pay one game at random from the battery (the standard solution to wealth-effect carryover between games) or pay all games and document the order. Always include a comprehension question with a remedial worked example branch before the live decision.

Sample size. Engel’s (2011) cross-study standard deviation of individual transfer share is roughly 0.25–0.30. A minimum detectable effect of 0.05 of the endowment at 80% power and α = 0.05 (two-sided) requires roughly n ≈ 400–500 per arm under simple random assignment. Once session-level intra-cluster correlation (typically ICC ≈ 0.02–0.05 in DG) is accounted for, inflate by the design-effect factor 1 + (m − 1)ρ where m is the average session size. Design power against the session ICC, not the individual ICC.

Caveats & common mistakes

Experimenter demand effects. The dictator game is unusually exposed to demand: zero is the self-interest answer, but any positive amount looks “generous.” If demand pushes transfers up — the typical direction — observed transfers are an upper bound on demand-free generosity. (The reverse claim is wrong.) Zizzo (2010) formalises experimenter demand; double-blind anonymity, neutral framing, and the de Quidt-style bounding approach are the standard mitigations.

External validity. Dictator transfers correlate positively but modestly with field altruistic behaviour. Levitt & List (2007) is the canonical skeptical reading; Benz & Meier (2008) provide the counterweight, showing that lab-measured donations correlate with real-charity donations from the same individuals (r ≈ 0.3–0.4). Report DG transfers as a measure of behaviour in the game context, not as a direct measure of “real-world altruism.”

Social norms vs. preferences. Krupka & Weber (2013) show that DG transfers track elicited social norms about appropriate giving very closely — meaning DG measures a composite of preference and perceived norm, not preference alone. Norm elicitation alongside the game (see the Krupka-Weber guide) is the standard fix where preference-versus-norm decomposition matters.

Enumerator effects. In face-to-face sessions, enumerators known to respondents, displaying expectations, or varying delivery across sessions introduce non-random noise. Standardised scripts, blind delivery where the enumerator does not see the allocation, and enumerator fixed effects in the analysis are the controls. In communities where enumerators may know participants, an enumerator masquerading as a recipient is a contaminating recipient pool — do not use.

Framing and labelling. Whether the game is described as “sharing,” “dividing,” “allocating,” or unlabelled affects outcomes. Neutral framing is the convention; if the research question is the framing effect itself, randomise the label and pre-register it (Branas-Garza, 2007).

Stake stability is contested. The conventional wisdom — that DG transfers are stake-invariant — is overstated. Engel (2011) reports a small but significant negative stake effect across the literature.

Analysis Guide

# Required columns: dictator_id, session_id, recipient_type, dictator_transfer,
# endowment, treatment, age, female, log_hh_expenditure
import numpy as np, pandas as pd
import statsmodels.formula.api as smf
import statsmodels.api as sm
from statsmodels.stats.proportion import proportions_ztest

# 1. Pre-filter to complete cases on outcome and treatment so all later focal-point
#    and regression statistics share the same denominator. Guard against
#    endowment = 0 which would silently produce inf/NaN under division.
df = df.dropna(subset=['dictator_transfer', 'endowment', 'treatment']).copy()
df = df[df['endowment'] > 0].copy()
df['transfer_share'] = df['dictator_transfer'] / df['endowment']
n = len(df)

# 2. Inspect distribution. The cross-study mean is ~0.28 (Engel 2011), with heavy
#    masses at 0 and 0.5 — bimodality is the rule. Mean alone hides the structure.
print(df['transfer_share'].describe(percentiles=[.1, .25, .5, .75, .9]))

# 3. Focal-point masses computed on integer arithmetic to avoid floating-point
#    failures (e.g., 5/9 == 0.5 is False under IEEE 754). The exact-half test is
#    'dictator_transfer * 2 == endowment'; the zero test compares the integer
#    directly. Bimodality is diagnosable via a dip test (R: diptest::dip.test).
share_zero = (df['dictator_transfer'] == 0).mean()
share_half = (df['dictator_transfer'] * 2 == df['endowment']).mean()
share_full = (df['dictator_transfer'] == df['endowment']).mean()
print(f'Mass at 0: {share_zero:.3f}   at 0.5: {share_half:.3f}   at 1: {share_full:.3f}')

# 4. Main effect with SESSION-CLUSTERED SEs (Frechette 2012). HC1/HC2 are wrong
#    for DG because participants in a session share enumerator, script, physical
#    space, and (under within-session matching) partner draws. For multi-arm
#    designs use C(treatment); for binary, bare treatment.
fit_ols = smf.ols('transfer_share ~ treatment + age + female + log_hh_expenditure',
                data=df).fit(
  cov_type='cluster', cov_kwds={'groups': df['session_id']})
print(fit_ols.summary())

# 5. Fractional logit (Papke & Wooldridge 1996) — the correct estimator for a
#    bounded fractional outcome on [0, 1] with mass at the corners. OLS gives
#    point estimates of the ATE that are consistent but can predict outside [0, 1];
#    fractional logit respects the bounds and is the field-standard alternative.
#    Use cluster-robust SEs at the session level.
fit_fl = smf.glm('transfer_share ~ treatment + age + female + log_hh_expenditure',
               data=df, family=sm.families.Binomial()).fit(
  cov_type='cluster', cov_kwds={'groups': df['session_id']})
print(fit_fl.summary())
# For two-limit Tobit or beta regression, see the R tab — Python lacks clean
# implementations for both (R: AER::tobit / censReg, betareg::betareg).

# 6. Extensive vs. intensive margin decomposition (Bardsley 2008; Engel 2011):
#    (a) Pr(gave anything > 0); (b) conditional mean transfer given gave > 0.
#    Use a logit for the extensive margin; fractional logit for the intensive.
df['gave'] = (df['transfer_share'] > 0).astype(int)
ext = smf.glm('gave ~ treatment + age + female + log_hh_expenditure',
            data=df, family=sm.families.Binomial()).fit(
  cov_type='cluster', cov_kwds={'groups': df['session_id']})
intens = smf.glm('transfer_share ~ treatment + age + female + log_hh_expenditure',
               data=df[df['gave'] == 1],
               family=sm.families.Binomial()).fit(
  cov_type='cluster', cov_kwds={'groups': df[df['gave'] == 1]['session_id']})
print('Extensive margin:'); print(ext.summary())
print('Intensive margin:'); print(intens.summary())

# 7. In-group / out-group premium. Within-subject (each dictator decides over
#    multiple recipient types): cluster at DICTATOR_ID, not session, because the
#    same dictator's decisions across recipient types are mechanically dependent.
fit_ig = smf.ols('transfer_share ~ C(recipient_type) + age + female',
               data=df).fit(
  cov_type='cluster', cov_kwds={'groups': df['dictator_id']})
print(fit_ig.summary())

# Required columns: dictator_id, session_id, recipient_type, dictator_transfer,
# endowment, treatment, age, female, log_hh_expenditure
library(estimatr)     # cluster-robust SEs
library(sandwich); library(lmtest)   # cluster-robust SEs for glm / tobit
library(AER)          # two-limit Tobit
library(betareg)      # beta regression (interior only)
library(diptest)      # bimodality diagnostic

# 1. Pre-filter once. Guard against endowment <= 0 which would silently
#    produce inf/NaN under division.
df <- df[complete.cases(df[, c('dictator_transfer', 'endowment', 'treatment')]), ]
df <- df[df$endowment > 0, ]
df$transfer_share <- df$dictator_transfer / df$endowment

# 2. Distribution.
summary(df$transfer_share)

# 3. Focal-point masses on integer arithmetic (avoids 5/9 == 0.5 -> FALSE).
mass0    <- mean(df$dictator_transfer == 0)
mass_half <- mean(df$dictator_transfer * 2 == df$endowment)
mass_full <- mean(df$dictator_transfer == df$endowment)
cat('Mass at 0:', mass0, ' at 0.5:', mass_half, ' at 1:', mass_full, '\n')
dip.test(df$transfer_share)   # significant -> reject unimodality

# 4. Main effect with SESSION-CLUSTERED SEs (Frechette 2012). HC1/HC2 are wrong
#    for DG because participants share enumerator, script, and matching.
fit_ols <- lm_robust(transfer_share ~ treatment + age + female + log_hh_expenditure,
                   data = df, clusters = session_id, se_type = "CR2")
summary(fit_ols)

# 5. Fractional logit (Papke & Wooldridge 1996) — quasi-binomial GLM for a
#    bounded fractional outcome on [0,1]. Cluster SEs at the session level via
#    sandwich::vcovCL.
fit_fl <- glm(transfer_share ~ treatment + age + female + log_hh_expenditure,
            data = df, family = quasibinomial(link = "logit"))
coeftest(fit_fl, vcov. = vcovCL(fit_fl, cluster = ~ session_id))

# 6. Two-limit Tobit for censoring at 0 and at endowment. AER::tobit is the
#    standard interface; coefftest gives cluster-robust inference.
fit_tobit <- AER::tobit(transfer_share ~ treatment + age + female + log_hh_expenditure,
                      left = 0, right = 1, data = df)
coeftest(fit_tobit, vcov. = vcovCL(fit_tobit, cluster = ~ session_id))

# 7. Beta regression for the interior only (after dropping 0s and 1s). Useful
#    when the corner mass is small; complements the Tobit / fractional logit
#    rather than replacing them.
df_int <- df[df$transfer_share > 0 & df$transfer_share < 1, ]
fit_beta <- betareg(transfer_share ~ treatment + age + female + log_hh_expenditure,
                  data = df_int)
coeftest(fit_beta, vcov. = vcovCL(fit_beta, cluster = ~ session_id))

# 8. Extensive vs. intensive decomposition (Bardsley 2008; Engel 2011).
df$gave <- as.integer(df$transfer_share > 0)
ext <- glm(gave ~ treatment + age + female + log_hh_expenditure,
         data = df, family = binomial())
coeftest(ext, vcov. = vcovCL(ext, cluster = ~ session_id))
intens <- glm(transfer_share ~ treatment + age + female + log_hh_expenditure,
            data = df[df$gave == 1, ], family = quasibinomial(link = "logit"))
coeftest(intens, vcov. = vcovCL(intens, cluster = ~ session_id))

# 9. In-group / out-group premium with within-subject variation in recipient
#    type — cluster at DICTATOR_ID, not session.
fit_ig <- lm_robust(transfer_share ~ factor(recipient_type) + age + female,
                  data = df, clusters = dictator_id, se_type = "CR2")
summary(fit_ig)

SurveyCTO / XLSForm

The dictator game runs as a structured CAPI module with stratified random assignment to recipient type. Standard pattern:

For double-blind anonymity, store dictator_transfer against an opaque session-time ID rather than the respondent’s name, and arrange payment through a third party who cannot link allocations back to individual respondents. For in-village recipient pools, use a private tablet entry mode (the dictator enters the allocation themselves on the tablet, with the screen turned away from the enumerator) to prevent enumerator knowledge of the allocation contaminating the recipient pairing.

Reading the output

• Mean transfer share: benchmark is 0.28 across studies (Engel, 2011 meta-analysis, 129 papers / 328 treatments). Means above 0.40 typically signal demand effects, imperfect anonymity, or a non-windfall endowment.
• Focal-point masses: report mass at 0 and at 0.5 (and at 1 separately). Engel (2011) reports modal mass at 0 (~36% of dictators) and a secondary mode at 0.5 (~17%). Heavy mass at 0.5 with low mass at 0 is a different behavioural pattern (norm compliance) than heavy mass at 0 with low mass at 0.5 (self-interest), even at similar means.
• Bimodality: diptest::dip.test in R returns a p-value for unimodality; p < 0.05 indicates the distribution is meaningfully bimodal — report this rather than the mean alone.
• Main treatment effect: from lm_robust(..., clusters = session_id) in R or cov_type='cluster' in Python. Read the treat coefficient, the CR2-robust SE, the 95% CI, and the p-value together. HC1/HC2 SEs are wrong for DG — participants share enumerator, script, and matching within a session (Fréchette, 2012).
• Fractional logit and Tobit: ATE direction should agree with OLS; magnitude can differ once boundedness is respected. Report fractional logit as the primary inferential estimator and OLS as a sanity check, or vice versa with a justified preference.
• Extensive vs. intensive: a treatment that moves the extensive margin (Pr[give > 0]) is qualitatively different from one that moves the intensive margin (mean | gave > 0). Report both.
• In-group premium (factor(recipient_type) coefficient with dictator-clustered SEs): co-ethnic / co-caste premia of 5–10 percentage points are typical in field studies; report the CI rather than the point estimate alone.
• Gender: Andreoni & Vesterlund (2001) is the canonical reference for the gender finding — women give more than men when giving is cheap, less when giving is expensive. Report the female coefficient with its CI; the direction is not universal.

References

Andreoni, J., & Miller, J. (2002). Giving according to GARP: An experimental test of the consistency of preferences for altruism. Econometrica, 70(2), 737–753. https://doi.org/10.1111/1468-0262.00302

Andreoni, J., & Vesterlund, L. (2001). Which is the fair sex? Gender differences in altruism. Quarterly Journal of Economics, 116(1), 293–312. https://doi.org/10.1162/003355301556419

Bardsley, N. (2008). Dictator game giving: Altruism or artefact? Experimental Economics, 11(2), 122–133. https://doi.org/10.1007/s10683-007-9172-2

Benz, M., & Meier, S. (2008). Do people behave in experiments as in the field? Evidence from donations. Experimental Economics, 11(3), 268–281. https://doi.org/10.1007/s10683-007-9192-y

Brandts, J., & Charness, G. (2011). The strategy versus the direct-response method: A first survey of experimental comparisons. Experimental Economics, 14(3), 375–398. https://doi.org/10.1007/s10683-011-9272-x

Charness, G., & Gneezy, U. (2008). What’s in a name? Anonymity and social distance in dictator and ultimatum games. Journal of Economic Behavior & Organization, 68(1), 29–35. https://doi.org/10.1016/j.jebo.2008.03.001

Cherry, T. L., Frykblom, P., & Shogren, J. F. (2002). Hardnose the dictator. American Economic Review, 92(4), 1218–1221. https://doi.org/10.1257/00028280260344740

Engel, C. (2011). Dictator games: A meta study. Experimental Economics, 14(4), 583–610. https://doi.org/10.1007/s10683-011-9283-7

Ensminger, J., & Henrich, J. (Eds.). (2014). Experimenting with social norms: Fairness and punishment in cross-cultural perspective. Russell Sage Foundation.

Falk, A., Becker, A., Dohmen, T., Enke, B., Huffman, D., & Sunde, U. (2018). Global evidence on economic preferences. Quarterly Journal of Economics, 133(4), 1645–1692. https://doi.org/10.1093/qje/qjy013

Forsythe, R., Horowitz, J. L., Savin, N. E., & Sefton, M. (1994). Fairness in simple bargaining experiments. Games and Economic Behavior, 6(3), 347–369. https://doi.org/10.1006/game.1994.1021

Fréchette, G. R. (2012). Session-effects in the laboratory. Experimental Economics, 15(3), 485–498. https://doi.org/10.1007/s10683-011-9309-1

Henrich, J., Boyd, R., Bowles, S., Camerer, C., Fehr, E., Gintis, H., & McElreath, R. (2005). “Economic man” in cross-cultural perspective: Behavioral experiments in 15 small-scale societies. Behavioral and Brain Sciences, 28(6), 795–815. https://doi.org/10.1017/S0140525X05000142

Hoffman, E., McCabe, K., & Smith, V. L. (1996). Social distance and other-regarding behavior in dictator games. American Economic Review, 86(3), 653–660. https://www.jstor.org/stable/2118218

Kahneman, D., Knetsch, J. L., & Thaler, R. (1986). Fairness as a constraint on profit seeking: Entitlements in the market. American Economic Review, 76(4), 728–741. https://www.jstor.org/stable/1806070

Krupka, E. L., & Weber, R. A. (2013). Identifying social norms using coordination games: Why does dictator game sharing vary? Journal of the European Economic Association, 11(3), 495–524. https://doi.org/10.1111/jeea.12006

Levitt, S. D., & List, J. A. (2007). What do laboratory experiments measuring social preferences reveal about the real world? Journal of Economic Perspectives, 21(2), 153–174. https://doi.org/10.1257/jep.21.2.153

List, J. A. (2007). On the interpretation of giving in dictator games. Journal of Political Economy, 115(3), 482–493. https://doi.org/10.1086/519249

Papke, L. E., & Wooldridge, J. M. (1996). Econometric methods for fractional response variables with an application to 401(k) plan participation rates. Journal of Applied Econometrics, 11(6), 619–632. https://doi.org/10.1002/(SICI)1099-1255(199611)11:6%3C619::AID-JAE418%3E3.0.CO;2-1

Zizzo, D. J. (2010). Experimenter demand effects in economic experiments. Experimental Economics, 13(1), 75–98. https://doi.org/10.1007/s10683-009-9230-z