Marital status and longevity in the United States population

A national probability sample of tens of thousands of adults, linked to official death records, is a strong basis for a descriptive comparison of death rates by marital status, and the adjustments for age, sex, income, education, race, and self-rated health are reasonable for the era. Social connection is never measured, so every conclusion about "isolation" rests on marital status as a stand-in. Marital status is recorded once, at baseline, and the never-married group is concentrated at ages when most people go on to marry, so the "never married" label is unreliable exactly where the paper claims the strongest effect. Nursing-home residents were excluded, which removes the sickest unmarried elderly and would tend to shrink any penalty at older ages — one possible reason the effect seems to fade with age in men. About 13,000 people are missing from the main model without explanation, and two tables are run on different samples. The follow-up years coincide with peak US AIDS mortality among unmarried men, which the authors name as the likely cause of the young-male infectious-disease excess but do not separate out.

Weighted logistic regression with odds ratios and 95% confidence intervals is appropriate for an eight-year binary death outcome, and the main never-married estimate (OR 1.58, CI 1.39–1.78) is precise and consistent with Johnson 2000 and Hu and Goldman 1990. Beyond that, the comparative claims are read off point estimates. Never-married versus widowed versus divorced intervals overlap and no contrast test is reported. The abstract's "significantly stronger for men than for women" has no interaction test behind it, and the male and female 19–44 intervals overlap. The male age gradient has no trend test. Every young-versus-middle-aged cause-specific pair overlaps. The model lets the never-married effect change with age and sex but forces the widowed and divorced effects to stay constant — so never-married is the only category that can look different across subgroups, which guarantees it will appear the most variable. The NHIS is a clustered, stratified sample and there is no sign of design-based variance estimation, so intervals are likely too narrow. Comparing odds ratios across age bands whose baseline mortality differs by two orders of magnitude, and concluding the effect is "stronger early in life," ignores absolute risk — a caveat the authors apply to their health-status strata and then drop for age. Sample sizes do not reconcile across tables (66,999 vs 79,713), yet Table 3 reproduces Table 2's subgroup estimates digit-for-digit. Two cells have confidence intervals inconsistent with their point estimates (male 65+; pulmonary, male 19–44). Twenty-one regressions run with no multiplicity adjustment. The health-habits rebuttal uses unadjusted percentages in groups with very different age structures, and smoking is available in the data but never entered as a covariate.

The paper calls marriage "a rough proxy for social connectedness" and then treats the proxy as the thing itself throughout the discussion and conclusions. The descriptive claim — unmarried people in 1989 died more by 1997 — is sound. The claims about isolation are not connected to anything in the data: no measure of contact, network, loneliness, or living arrangement exists in the analysis, even though the survey records household composition and could have counted children in the home, the mechanism the authors propose. The exposure is frozen at baseline, so for young adults the label marks who was still single at that age in 1989, not eight years of unmarried life. The claim that isolation is stronger early in life depends on a young-male excess the authors attribute to HIV; the claim that it reaches beyond heart disease depends on infectious and external-cause deaths the authors attribute to HIV and risk behaviour. Once those are set aside, the only non-cardiac category without a competing explanation is an undefined "other" bucket. The comparison to blood pressure and cholesterol equates a population marker for an unmeasured bundle of factors with individual risk factors that have known causal pathways.

The descriptive result is well established and the limitations section is honest about baseline-only measurement, cohort effects, and the impossibility of establishing causation. The conclusions do not carry those hedges. The isolation framing works no matter what the data show: a penalty concentrated in the old would have been read as cumulative isolation, one confined to heart disease would have confirmed Lynch 1977. No pattern could have counted against it. The paper names HIV as the likely cause of the young-male excess and then uses that same excess as evidence that isolation is "comparatively stronger early in life." The ranking of never-married above widowed and divorced is hedged in the results (intervals overlap) and asserted without qualification in the abstract and conclusions. The rebuttal of the risky-behaviour explanation cites smoking, drinking, and weight — habits relevant to heart disease and cancer — when the excess deaths needing explanation are from infection and accidents, homicide, and suicide.

Data are public federal datasets and the authors declare no funding and no conflicts. The main model contains about 13,000 fewer people than the stated sample and only a third of the shortfall is explained; the second model uses a different sample without comment. The six cause-of-death categories are not mapped to death-certificate codes, and the "other" category holding 15% of deaths is defined only as everything else. The covariate list differs between text, table, and footnotes. The health-habit figures come from an undescribed tabulation. No code is released. Two table entries are internally inconsistent and the follow-up end year is given as both 1996 and 1997. The limitations section names the biggest weakness — one-time measurement of marital status — but omits the untested ranking, the multiple comparisons, and the sample discrepancies.

The core findings rest on the authors' own data, not on citations. A string of twelve references offered as studies showing that social networks lengthen life includes a paper on medieval London widows, a mathematical population model, and two demographic papers on marriage duration. Two references on injection drug users are cited for claims about self-rated health and about the never-married population generally. The conclusion that the findings "challenge the belief" that isolation acts on the heart is a straw man: the studies it cites for that belief (Berkman and Syme 1979, House 1982, Seeman 1987) were all-cause mortality studies. Standard literature on selection versus protection (Goldman 1993; Lillard and Panis 1996)Lillard and Panis 1996) and prior use of the same survey-to-death-index linkage for this question (Rogers 1995; Rogers, Hummer and Nam 2000) is absent; the paper says it is "not aware" of such prior use.

No funding, no declared conflicts, academic authors, public government data the authors did not collect. There is no commercial or advocacy interest in the result, the paper draws no marriage-policy conclusions, and the discussion foregrounds selection, HIV, and cohort effects as alternatives to a protective effect of marriage.