Measured treatment differences between sexes and genders: A scoping review

A scoping review is reasonable for mapping an under-studied area, and the procedural elements are sound: both authors independently screened studies against pre-specified criteria, disagreements were resolved through discussion, and quality appraisal used established JBI checklists. But the paper's conclusions go well beyond mapping. Claims like "men and women are frequently treated differently" and "females were consistently less likely to receive invasive treatments" require meta-analytic pooling, publication-bias assessment, and heterogeneity analysis — none of which a scoping review provides.

The vote counting conflates studies finding women receive more treatment with those finding women receive less. At least nine of 38 case series performed no multivariate analysis, meaning their reported differences may reflect age, comorbidity, or disease severity rather than sex-based treatment decisions. The claim that women with "comparable clinical characteristics" receive less treatment fails for the four comparisons in Table 1 that used unadjusted analyses. One included study (Shpiner 2019) explicitly found that women's lower procedure rates partly reflected patient preference — a confounder unmeasured in the other studies.

Twenty-six of 41 studies came from the United States and 15 from cardiovascular medicine, yet the conclusions refer to "healthcare systems" without qualification. Publication bias is unaddressed.

The review reports no statistical tests — no pooled effect sizes, no heterogeneity measures, no funnel plots, no sensitivity analyses. Its central quantitative claims (33 of 38, 25 of 29) are simple vote counts.

Vote counting is recognized in the evidence-synthesis literature as unreliable for drawing conclusions about the direction or consistency of effects. A study testing 19 diabetes care measures and finding none different (Bak 2023) counts as one "no difference" study. A study testing five outcomes and finding one difference counts as one "significant" study. Studies running many comparisons have a higher chance of producing at least one difference by chance, but the review counts each study once regardless.

Tables 1 and 2 do report individual effect sizes with confidence intervals, which is useful. The reported odds ratios range from 0.29 (women far less likely to receive endoscopic hernia repair) to 1.71 (women more likely to receive anti-dementia medications). But the narrative never engages with these magnitudes. A reader of the abstract learns that most studies found a difference but not whether those differences were clinically meaningful. The tables also mix adjusted and unadjusted estimates without distinguishing them in the text, and the narrative treats both as evidence about patients with "comparable clinical characteristics."

Every core claim stretches beyond what the evidence supports. The 33-of-38 count conflates different directions and magnitudes into a single number that reads as evidence of one phenomenon. The 25-of-29 multivariate figure sounds more rigorous but treats a study adjusting only for age the same as one adjusting for age, race, comorbidities, insurance, and disease severity.

The claim that women "consistently" receive fewer invasive procedures holds for 13 of 16 comparisons in Table 1, but the three exceptions are not trivial — women were more likely to receive liver ablation (a large effect in the opposite direction) and equally likely to proceed with deep brain stimulation after referral. The claim that women receive less guideline-compliant therapy reflects 14 of 24 comparisons in Table 2, but four found women receiving more (anti-dementia medications, blood pressure control, smoking cessation counseling) and six found no difference. The conclusion reports only the majority direction.

The overarching claim — that men and women are "frequently" treated differently — implies something about how often differences occur across all of healthcare, but the review has no denominator. Forty-one studies across all specialties and countries over five years, drawn primarily from US cardiology, cannot establish that frequency.

The discussion acknowledges that "it is not possible to determine whether this was as a result of inequities or due to another cause," but the conclusion drops this qualifier and states flatly that men and women are frequently treated differently. The conclusion claims women were "less likely to receive guideline-compliant therapy" without noting that four of twenty-four comparisons found the opposite. Counterevidence reported in the body does not survive into the abstract or conclusions.

The assumption that the ratio of positive studies reflects reality is untested. Published studies designed to detect sex differences in treatment are more likely to find them and more likely to be published when they do. The review does not address this selection effect.

The paper offers only two specific mechanisms for observed disparities: a 1999 study on physician communication (Elderkin-Thompson & Waitzkin 1999) and patient preference (from one included study). It does not engage with the clinical literature on sex-based differences in disease presentation, anatomy, or drug metabolism that might explain some treatment variation as medically appropriate.

The review reports its search terms, eligibility criteria, and screening process in detail. Supplementary files are provided. Conflict of interest and funding are clearly disclosed (none of either). The JBI quality appraisal results are reported for each study.

What is missing: no pre-registration, no analysis code, and the full search strings are not reproduced in the main text. The limitations section acknowledges retrospective designs, incomplete confounder adjustment, and US-dominated data, but does not address publication bias or the known weaknesses of vote counting — the two most consequential threats to the paper's conclusions.

The review cites Raine (2000) as finding that males were more likely to receive renal transplantation while females were more likely to receive liver transplantation. But the review's Table 1 shows the opposite for liver transplantation: both Darden (2021) and Listabarth (2022) found females were less likely to receive liver transplants. The paper does not acknowledge this contradiction.

Elderkin-Thompson & Waitzkin (1999) is cited as explaining why physicians may treat women differently — attributing symptoms to "over-anxiousness" and making more diagnostic errors. This 27-year-old finding is presented as a current mechanism without noting the temporal distance. It is one of only two specific explanations offered for the observed disparities.

The introduction devotes substantial space to intersectionality and COVID-19's effects on academic medicine (Crenshaw 1991, Woitowich 2021, Laster Pirtle & Wright 2021), but the review found almost no intersectional data and the pandemic framing has no connection to the measured outcomes. These citations set expectations the review cannot fulfill. Meanwhile, the clinical literature on sex differences in cardiovascular anatomy, drug metabolism, and disease presentation — which might explain some treatment variation as medically appropriate — is entirely absent.

Both authors are at UK public universities. They received no funding and declared no competing interests. Independence is not a concern.