Law and Norms: Lane, Nosenzo & Sonderegger (2023)

What this is. This is an LLM-distilled skeleton of Lane, Nosenzo, and Sonderegger (2023); read the original to replicate or extend.

TL;DR

Lane, Nosenzo, and Sonderegger develop a legal-threshold identification strategy to test whether laws causally influence social norms. They study laws regulating behavior through thresholds (age of consent, legal drinking age, maximum undeclared cash import, BAC drink-driving limit, motorway speed limit), measuring perceived appropriateness on either side of each threshold in incentivized vignette experiments with 1,248 UK subjects across three samples. Under the assumption that norms would otherwise vary continuously near the threshold, a discontinuity identifies an expressive effect of law. They find large, statistically significant drops for age of consent, alcohol sales to minors, and undeclared cash imports, with weaker effects for drink driving and speeding. Four follow-up experiments with 5,771 additional subjects in the UK, US, and China find that placebo thresholds usually have smaller effects, though there are exceptions for driving vignettes; this provides little support for focal-point or information-transmission explanations. Ratings of prosocial traits also shift at legal thresholds, consistent with the authors’ preferred social-image account. In a CANO vignette where breaking the rule protects a third party, honesty ratings rise significantly; the authors say this casts doubt on a rule-following meta-norm explanation.

Core results

#	Result	Locator	Magnitude as reported
R1	Age of consent: strong norm discontinuity at legal threshold	Table 2, pp. 1274-1275; Fig. 1, p. 1272	beta2 = -0.778 (students, SE 0.184); -0.890 (gen pop 2019, SE 0.127); -0.803 (2021 first-order, SE 0.119); -0.813 (2021 second-order, SE 0.138). The paper describes the student estimate as highly significant.
R2	Alcohol to youth: large norm discontinuity, largest in the student and 2021 samples	Table 2, pp. 1274-1275; Fig. 1, p. 1272	beta2 = -1.035 (students, SE 0.138); -0.920 (gen pop 2019, SE 0.118); -1.047 (2021 first-order, SE 0.116); -1.137 (2021 second-order, SE 0.113). The student estimate is highly significant.
R3	Cash at customs: strong norm discontinuity	Table 2, pp. 1274-1275; Fig. 1, p. 1272	beta2 = -0.866 (students, SE 0.132); -0.948 (gen pop 2019, SE 0.124); -0.821 (2021 first-order, SE 0.129); -0.971 (2021 second-order, SE 0.127). The student estimate is highly significant.
R4	Drink driving: weaker norm discontinuity	Table 2, pp. 1274-1275	beta2 = -0.326 (students, SE 0.178, p=0.068); -0.522 (gen pop 2019, SE 0.143); -0.487 (2021 first-order, SE 0.143); -0.542 (2021 second-order, SE 0.139). The student estimate is significant at 10 percent; the general-population estimates are strongly significant.
R5	Speeding: weak effects, insignificant for student sample	Table 2, pp. 1274-1275	beta2 = -0.103 (students, SE 0.107, not significant); -0.461 (gen pop 2019, SE 0.127); -0.592 (2021 first-order, SE 0.097); -0.577 (2021 second-order, SE 0.109). The paper reports strong significance for the general-population estimates.
R6	Placebo thresholds usually produce smaller discontinuities	Fig. 2, p. 1280; discussion pp. 1279-1281; Appendix F	Under Krupka-Weber, the cash-at-customs placebo discontinuity is 0.22 versus 0.88 at the legal threshold; the legal-placebo difference has p=0.000. The cash placebo itself has p=0.054. Placebos at age-of-consent and alcohol-to-youth thresholds are not significant under either method; the paper also reports exceptions for driving vignettes.
R7	Perceived trustworthiness and honesty drop sharply at legal threshold (Exp 2)	Fig 3, Appendix G, p. 1282-1283	Trustworthiness drops 0.45-0.63 units; honesty drops 0.51-0.81 units; altruism drops 0.26-0.42 units across high-effect vignettes (all p <= 0.009)
R8	”Bad” law (CANO): upward discontinuity in honesty weighs against rule-following explanation (Exp 3)	Fig. 4, p. 1287; discussion pp. 1286-1287; Appendix I	Honesty +0.36 (p=0.002); trustworthiness +0.11; altruism +0.17 (both n.s.); rule-compliance shows near-zero discontinuity (-0.04). The authors say this casts doubt on the meta-norm explanation.
R9	Legal-threshold effects are larger for high-effect vignettes than driving vignettes	Table 2 discussion, pp. 1274-1275	Chow tests: no differences among age-of-consent, alcohol-to-youth, and cash-at-customs coefficients in any sample (all p >= 0.136); students: high-vs-low comparisons all p <= 0.028 except drink-driving vs age-of-consent p = 0.124; 2019 population: all p <= 0.088; 2021 first-order: alcohol vs drink-driving and speeding both p <= 0.009; 2021 second-order: comparisons p <= 0.056 except comparisons involving age-of-consent (p = 0.256)
R10	Smaller prosocial-trait discontinuities for speeding and drink driving (Exp 2)	Fig. 3, p. 1283; discussion pp. 1283-1284	Speeding drops: honesty 0.37, trustworthiness 0.24, altruism 0.20; drink driving drops: honesty 0.42 (p=0.000), altruism 0.16 (p=0.079), trustworthiness 0.15 (p=0.130)
R11	Expressive effects also appear in China, where rule of law is weaker	Experiment 4 discussion, pp. 1287-1288; sample size in Table 3, p. 1277	248 Chinese students; the paper reports that effects remain strong in some, but not all, situations; exact estimates are relegated to online Appendix J
R12	Perceived intentionality and detectability moderate legal-threshold effects	Section III discussion, p. 1276; online Appendix E is referenced	Effects are generally weaker for subjects who think illegal behavior may be unintentional or difficult to measure; the main-text discussion gives no coefficient magnitudes; evidence for police tolerance as a moderator is weaker

Overall. The authors’ preferred explanation is that laws shape norms through social-image signaling: illegality can signal lower prosociality, with the strongest norm effects in domains where illegal behavior is perceived as intentional and detectable. Trait ratings and the upward honesty discontinuity under the CANO are consistent with this account. They argue that laws can harness social incentives to complement formal deterrence, an implication rather than a directly measured behavior outcome. The paper also presents a conformity-based model that can explain the findings under additional assumptions, so the experiments cast doubt on a simple rule-following account without ruling out every conformity explanation.

Theory / model

The model (Section I, pp. 1260-1264) adapts the social-image framework of Benabou and Tirole (2006, 2011). An individual with privately known type theta (measuring prosociality) faces an opportunity o drawn from a distribution with density g(.) and full support [o_min, o_max] with o_min > 0, where o is the magnitude of the negative externality imposed on others. The individual can seize or leave the opportunity. A law sets a threshold o-bar above which seizing the opportunity is illegal; if caught (with probability p), the individual incurs a material penalty K.

Utility. Utility depends on the material payoff, the psychological cost of imposing externalities, and social esteem from observers’ inferences about type (eq. 1, p. 1260):

u_a(o;\theta) = (t - \theta o - pK I_{o>\bar{o}})a + S(o,a), \tag{1}

where t is the material gain, $I_{o>\bar{o}}$ is an indicator for illegal action, a = 1 if the opportunity is seized (a = 0 otherwise), and S(o, a) is the social esteem accruing to the individual. Social esteem equals observers’ expectation of the individual’s type upon observing opportunity o and action a (pp. 1260-1261):

$S(o,1) \equiv E(\theta \mid o, a=1), \qquad S(o,0) \equiv E(\theta \mid o, a=0).$

In equilibrium without a law, the esteem values are conditional means above and below the marginal type who takes opportunity o (eq. 2, p. 1261):

S(o,1)=\mathcal{M}^-(\hat{\theta}_o), \qquad S(o,0)=\mathcal{M}^+(\hat{\theta}_o). \tag{2}

Absence of law (Proposition 1, p. 1262). When no law sets a threshold (p = 0), equilibrium esteem is determined by the highest type theta-hat who seizes opportunity o, defined by the indifference condition (eq. 3, p. 1262):

t - \hat{\theta}_o \, o - \Delta(\hat{\theta}_o) = 0, \tag{3}

where $\Delta(\hat{\theta}_o) \equiv \mathcal{M}^+(\hat{\theta}_o) - \mathcal{M}^-(\hat{\theta}_o)$ is the esteem gap, with $\mathcal{M}^-(\theta_o) \equiv E(\theta \mid \theta < \theta_o)$ and $\mathcal{M}^+(\theta_o) \equiv E(\theta \mid \theta > \theta_o)$. Since theta-hat is continuously decreasing in o, S(o, 1) is also continuously decreasing in o: without law, norms do not create sharp distinctions between arbitrarily close behaviors.

Presence of law (Proposition 2, p. 1263). When a law sets a threshold o-bar, legal sanctions create a payoff discontinuity. The threshold type for illegal actions solves (eq. 5, p. 1263):

t - pK - \tilde{\theta}_o \, o - \Delta(\tilde{\theta}_o) = 0. \tag{5}

Since theta-hat (highest type taking legal action just below o-bar) always lies strictly above theta-tilde (highest type taking illegal action just above o-bar), and $\mathcal{M}^-(\cdot)$ is increasing, the esteem function exhibits a downward discontinuity at o-bar (eq. 4, p. 1263):

S(o,1) = \begin{cases} \mathcal{M}^-(\hat{\theta}_o), & \text{if } o \le \bar{o}; \\ \mathcal{M}^-(\tilde{\theta}_o), & \text{if } o > \bar{o}, \end{cases} \tag{4}

The corresponding equilibrium esteem from leaving the opportunity is (also eq. 4, p. 1263):

$S(o,0) = \begin{cases} \mathcal{M}^+(\hat{\theta}_o), & \text{if } o \le \bar{o}; \\ \mathcal{M}^+(\tilde{\theta}_o), & \text{if } o > \bar{o}. \end{cases}$

with jump:

$\lim_{\epsilon\to 0}\bigl[S(\bar{o}-\epsilon,1) - S(\bar{o}+\epsilon,1)\bigr] = \mathcal{M}^-(\hat{\theta}_{\bar{o}}) - \mathcal{M}^-(\tilde{\theta}_{\bar{o}}) > 0.$

Proposition 3 (p. 1264) extends the result to distant observers (who see the criminal record but not the action directly): the discontinuity holds even when K = 0, since visibility of illegal behavior to a wider audience is itself a mechanism.

Method

The empirical approach (Section II, pp. 1265-1270) exploits laws with threshold rules to identify the causal effect of law on norms, using a design analogous to regression discontinuity. The identifying assumption is that the social norm function S(.) is continuous in the vicinity of the legal threshold absent the law’s expressive effect. Under this assumption, any discrete jump in measured norms at the legal threshold is causally attributable to the law (p. 1265).

The causal estimand is the difference between perceived esteem for legal and illegal actions at the threshold, equal to the left-minus-right limit of the norm function (eq. 6, p. 1266):

\left.\left[S(o,1 \mid o \le \bar{o})-S(o,1 \mid o>\bar{o})\right]\right|_{o=\bar{o}} = \lim_{\epsilon\to 0}\left[S(\bar{o}-\epsilon,1)-S(\bar{o}+\epsilon,1)\right]. \tag{6}

Norm elicitation. Two incentivized methods from Krupka and Weber (2013) and Bursztyn, Gonzalez, and Yanagizawa-Drott (2020) are used:

• Krupka-Weber method: subjects rate vignette behavior on a four-point scale (very/somewhat socially appropriate or inappropriate) and earn a bonus when their response matches the modal response in their sample. This coordination game incentivizes truthful second-order belief reporting.
• Opinion matching method: a first group states personal appropriateness opinions (unincentivized); a second group guesses the first group’s modal response for a financial bonus. This elicits second-order beliefs without legality as a coordination device.

Experimental design. Subjects are randomly assigned between-subjects to one of 4 or 8 versions of each vignette, varying the behavior’s distance from the legal threshold (e.g., age of the younger person in the age-of-consent vignette being 1-4 months above or below the threshold). The random assignment of subjects to versions means the identification design is randomized, not observational; the RDD-analogy is in the analysis, not in whether subjects select their treatment. Prior work such as Tankard and Paluck (2017) and Casoria, Galeotti, and Villeval (2020) exploited natural changes in existing laws to study law’s effect on norms; those designs face the challenge that simultaneous events may confound the measured effect. The present design instead uses legal thresholds, requiring only the local continuity assumption rather than assuming all other norm-relevant factors are unchanged by a legislative change.

Samples. The main experiment (Section II.C, pp. 1269-1270, Table 1, p. 1270) ran between September 2017 and March 2021 with 1,248 UK participants across three samples: 197 students (Krupka-Weber, 2017), 375 representative general-population subjects (Krupka-Weber, 2019), and 676 representative general-population subjects (opinion matching, 2021). Robustness experiments added 5,771 subjects (Table 3, p. 1277): 1,554 UK general-population (Exp 1 placebo), 2,767 UK general-population (Exp 2 prosocial traits), 1,202 US general-population (Exp 3 bad law), and 248 Chinese students (Exp 4 weak rule of law).

Empirical specifications

Main regression (eq. 7, p. 1273). For each vignette and sample, OLS is estimated with heteroskedasticity-robust standard errors. The corresponding randomized UK groups contain 197 students, 375 general-population subjects in 2019, and 332 first-order and 334 second-order respondents in the 2021 samples:

s(o_i) = \alpha + \beta_1(T - o_i) + \beta_2 \, \text{Illegal}_i + \beta_3(T - o_i) \times \text{Illegal}_i + \epsilon_i, \tag{7}

where $s(o_i)$ is subject i’s social appropriateness evaluation (coded +1 to -1 for four-point scale), $(T - o_i)$ is the signed distance from the legal threshold T (positive for legal, negative for illegal actions), $\text{Illegal}_i$ is a dummy equal to one for the vignette version describing illegal behavior, and $\beta_2$ is the key coefficient of interest: the estimated norm discontinuity at the legal threshold (the causal effect of law on normative appropriateness). Regressions for the two general-population samples include demographic controls (age, gender, income); no controls were collected for the student sample.

For the age-of-consent and alcohol-to-youth vignettes, below-threshold behavior is illegal and the paper codes signed distance as $o_i-T$; it uses $T-o_i$ for the other three. The randomized vignette versions require no fixed effects. The Table 2 note reports that bootstrapped standard errors give very similar results (pp. 1274-1275).

Identification check. Chow tests confirm no statistically significant differences in $\beta_2$ across the three high-effect vignettes (age of consent, alcohol to youth, cash at customs) within each sample (all p >= 0.136), but statistically significant differences between the first group (high effect) and the second group (drink driving, speeding), supporting the model’s prediction that intentionality and law-enforcement detectability moderate the effect size (p. 1273-1276, Appendix E).

Placebo regression (Exp 1). An extended version of equation (7) adds dummy variables for a placebo threshold placed 5-6 units from the legal threshold and its interaction with threshold distance. The placebo produces no significant discontinuities in four of five vignettes (Krupka-Weber method); the legal-threshold discontinuity is significantly larger than the placebo in all five cases where a comparison is possible (p. 1278-1280, Appendix F).

The main-text robustness check is described as re-estimating (7) with a placebo-threshold indicator in place of the legal-status indicator (written out from the description in footnote 21, p. 1275):

$s(o_i)=\alpha+\beta_1(T-o_i)+\beta_2\,\text{Placebo}_i+\beta_3(T-o_i)\times\text{Placebo}_i+\epsilon_i.$

The placebo experiment recruited 1,554 UK general-population respondents (Table 3, p. 1277); the versions were randomly assigned. It uses the same OLS setup and robust standard-error treatment as the main specification.

Prosocial-traits regression (Exp 2). The same regression specification is applied to subjects’ ratings of the likelihood that the vignette person engages in trustworthy, honest, and altruistic behavior, using the opinion-matching method with 1,984 incentivized and 783 unincentivized UK general-population subjects. Each subject sees one version of one target vignette, randomly assigned. Results (Appendix G, p. 1282-1283): statistically significant discontinuities in trustworthiness and honesty across all high-effect vignettes (all p <= 0.009), confirming the social-image mechanism.

Here the dependent variable in (7) is the +1 to -1 rating for each trait. The high-effect vignette discontinuities range from 0.45 to 0.63 for trustworthiness, 0.51 to 0.81 for honesty, and 0.26 to 0.42 for altruism (Figure 3 discussion, pp. 1282-1283). The smaller speeding and drink-driving estimates are reported in R10 (Figure 3 discussion, pp. 1283-1284). For the CANO bad-law vignette, subjects were randomly assigned across versions; the sample contained 1,202 US respondents (802 incentivized and 400 nonincentivized; text pp. 1285-1286). Figure 4, p. 1287 reports its discontinuities for the prosocial traits and rule compliance.

Datasets used

Dataset	Role in paper	Wiki page
Original vignette experiment, UK samples (1,248 subjects, 2017-2021)	Main experiment measuring social norm functions; Krupka-Weber and opinion-matching methods	no page yet
Robustness experiment 1 (1,554 UK subjects, 2021)	Placebo-threshold test via Prolific	no page yet
Robustness experiment 2 (2,767 UK subjects, 2021)	Prosocial-traits elicitation via Prolific	no page yet
Robustness experiment 3 (1,202 US subjects, 2022)	“Bad law” CANO vignette via Prolific	no page yet
Robustness experiment 4 (248 Chinese students, 2017)	Weak-rule-of-law generalizability test	no page yet

All data are author-collected online vignette experiments; replication data are deposited at https://doi.org/10.3886/E182995V1.

When to read the full paper

Read this paper to understand the expressive function of law from a causal empirical standpoint. The theoretical model (Section I) is compact and shows formally how a social-image mechanism (Benabou and Tirole 2011) predicts exactly the pattern observed. The norm-elicitation methods (Section II.B) using Krupka and Weber (2013) and Bursztyn, Gonzalez, and Yanagizawa-Drott (2020) are carefully contrasted. The online appendices (A-K) contain full proofs, vignette wordings, robustness analyses, regression tables, and an alternative conformity-based model. Figure 1 (p. 1272) gives a visual overview of all five norm functions across all three UK samples; Table 2 (pp. 1273-1275) gives the full regression results.

Attribution and rights

Lane, T., Nosenzo, D., and Sonderegger, S. (2023). “Law and Norms: Empirical Evidence.” American Economic Review 113(5): 1255-1293. https://doi.org/10.1257/aer.20210970

This page is an LLM-distilled extract (claude-sonnet-4-6, 2026-06-25). Not human-verified; not reproduced. The source article is paywalled; no CC licence is recorded in Crossref metadata. An open author manuscript is available at https://eprints.ncl.ac.uk/file_store/production/293182/ACD73151-8B74-4985-A1E4-B8D65A151BE8.pdf. Replication data are available at https://doi.org/10.3886/E182995V1.