AI Review Summary

The study compares all French-speaking and German-speaking workers across Switzerland, meaning that for unilingual cantons, language is perfectly confounded with the canton itself. Canton-level differences in economic structure, local labor regulations, or cost of living might fully explain the findings. While canton-by-year fixed effects are used in a robustness check, this specification relies entirely on within-canton language variation (e.g., migrants) or bilingual cantons, which may not generalize to the broader population. The authors should explicitly address this canton-language confounding as a limitation.

The authors measure the psychological cost of the hours gap (overwork) but do not include absolute actual hours worked as a control. Without a baseline controlling for actual hours worked and its interaction with the French indicator, it is impossible to determine whether the observed cultural penalty is due to deviations from the contract (the hours gap) rather than a general cultural disutility for working longer absolute hours. I recommend including actual hours worked and its interaction with the language indicator as controls to isolate the effect of the hours gap.

The authors claim that the concentration of the effect among part-time workers supports a general contractual-salience mechanism where part-time contracts more explicitly demarcate the work-leisure boundary. However, Table 5 shows that for women, the cultural interaction is virtually identical for part-time (-0.031) and full-time (-0.032) workers. The claim that contractual salience is the primary driver is not logically supported for women. I suggest revising the language in the abstract and introduction to reflect that this mechanism appears to operate exclusively for men, rather than treating it as a universal phenomenon.

In Section 5.7.2, the authors use two-sided equivalence tests to argue that the behavioral differential is smaller than the psychological differential, using the numerical value of the work-life interference cultural penalty (0.038) as the equivalence margin for the hours-gap persistence coefficient. This is logically flawed because the two coefficients have fundamentally different units (points on a 0–10 scale per hour of overwork versus hours of overwork in year t per hour of overwork in year t-1). Comparing their magnitudes directly is mathematically invalid. I recommend removing this equivalence test or replacing it with an economically meaningful, unit-appropriate behavioral threshold.

In Section 5.8.4, the authors claim there is a regression kink at the contractual boundary, arguing that the cultural interaction switches on above the contract because the interaction is significant above the contract but not below it. However, Table 10 shows that the point estimates for the interaction are nearly identical below (-0.035) and above (-0.031) the contract. The lack of statistical significance below the contract is driven by the much smaller sample size, not an absence of effect. Concluding that an effect is absent simply because it is not statistically significant, especially when the point estimate is identical to the significant condition, is a logical fallacy. I suggest revising the interpretation to acknowledge that the slope difference is consistent across both sides of the contract.

Figure A.8 visually depicts a similar slope below the contract for both language groups, and the caption repeats this claim. This contradicts the quantitative findings in Table 10, which reports a Below Contract interaction of -0.035, a value larger in magnitude than the Above Contract interaction of -0.031. This indicates that the slope difference between French and German speakers is actually slightly larger below the contract than above it. The figure and its caption do not accurately represent the underlying data and should be revised.

The dismissal of the severe pre-trends identified in the event study (Appendix C.1) relies on a logical fallacy regarding panel data estimators. The authors argue that the pre-trends do not threaten the main fixed-effects specification because the event study uses a binary onset indicator while the main model uses continuous within-person variation. However, if time-varying unobservables drive a diverging work-life interference trajectory years prior to the actual onset of overwork, the continuous fixed-effects estimator will also absorb this endogenous trajectory, biasing the main interaction coefficient. The authors must either provide a more robust identification strategy that accounts for these diverging pre-trends or substantially temper the causal interpretation of the main fixed-effects estimates, explicitly acknowledging that the continuous measure is likely capturing the same selection or anticipatory effects seen in the event study.

The use of a post-hoc power analysis in Section 5.5 to justify the non-significant triple interaction is statistically invalid. Calculating power using the observed effect size and sample variance is mathematically redundant with the p-value and provides no genuine information about the study's ability to detect a true effect. The authors should remove the post-hoc power calculation and instead discuss the precision of the estimate using the confidence intervals, or provide an a priori power analysis based on a pre-defined, theoretically justified minimum detectable effect size.

The manuscript lacks a data and code availability statement, which is critical for verifying the extensive panel data econometrics and custom data processing pipelines used. To ensure the computational reproducibility of the findings, the authors must provide the analysis scripts, specify the software and package versions used, and detail the exact procedures for cleaning, filtering, and merging the Swiss Household Panel waves.

The abstract and introduction frame the cultural penalty of overwork as a general phenomenon among German-speaking workers, with a secondary note that it is "concentrated among part-time workers." However, Table 5 demonstrates that for full-time men—the largest demographic subgroup in the sample (N=30,494)—the cultural interaction is precisely zero. Framing the main result as a broad cultural difference overgeneralizes the findings, as the cultural penalty is entirely absent for a massive segment of the workforce. The manuscript should be revised to accurately reflect that the cultural amplification of overwork costs is specific to part-time workers and women, rather than a universal feature of the German-speaking labor market.

The hours gap is calculated as the difference between self-reported actual hours and self-reported contractual hours. While the authors acknowledge that this measure is endogenous and address potential reporting bias in the dependent variables, they do not address the potential for culturally differential recall bias in the independent variable. If German-speaking workers, who possess stricter norms regarding the work-leisure boundary, are more meticulous in tracking and reporting minor deviations from their contract than French-speaking workers, the observed interaction could partially reflect a cultural difference in measurement precision. The discussion of limitations should address how differential measurement error in the reporting of actual hours might influence the interaction estimates.