'Til Death Do Us Part: Marital Disruption and Mortality

The longitudinal panel is an advance over the cross-sectional death-certificate work that preceded it. For the descriptive question — do married people in this cohort die at lower rates than unmarried people of the same age and year — the design is sound and the sample represents the US population of the era. But the paper's stated focus is the protective effect of marriage, and the design gives no purchase on that. There is no pre-marriage baseline for health or behavior, no within-person comparison, and no cause of death to check the prediction that marriage reduces men's deaths from accidents and violence. Marriage duration, for most people, is age minus age at marriage, so the "cumulating benefit" is identified by comparing people who married young with people who married late — and the paper's own footnote acknowledges that frail and risky people leave long marriages through death and divorce. Measurement problems compound this. Every one of the 857 deaths occurred before the retrospective marital history was collected, so decedents' marital status comes from annual proxy reports. A third of death dates are unverified. People who dropped out of the survey are treated as alive, which likely undercounts deaths after divorce. Income is measured in the year of death, when terminal illness has already reduced earnings.

The model is competent: a Gompertz-type proportional hazards specification with a piecewise-linear age spline, time-varying covariates, and correct handling of left truncation. Two headline sex differences fail on the reported coefficients. The duration slope is −0.0148 (SE .0044) for women versus −0.0085 (SE .0030) for men; the difference is roughly 1.2 standard errors, yet the paper calls it "significantly larger for women." The zero-duration marriage effect is 0.39 (SE .17) for men versus −0.04 (SE .25) for women; the difference is about 1.5 standard errors, yet the paper describes "strikingly different patterns." No pooled model with sex interactions appears anywhere. All mediation claims are inferred by watching a coefficient shrink when covariates enter, with no test of the change or of its sex difference. Deaths are never reported by marital status. Back-calculating from the standard errors suggests the "uniquely disadvantaged" separated-women result rests on roughly a dozen deaths, and the top-quartile income slope for women (−3.45, SE 1.74) implies an implausible 30% mortality reduction per 10% income rise, which points to sparse data rather than a real gradient. Several null results are treated as positive findings without power discussion. Table 5 contains sign flips between adjacent models with identical standard errors and a −0.75 coefficient (z ≈ 4.8) carrying no significance stars, so the printed numbers cannot be taken at face value.

"Protection" is never measured; the data contain a marital label and a death. Social integration is measured by counting other adults and children in the house, though the paper's own footnote says most social integration comes from ties outside the household, and the count lumps a cohabiting partner with a parent who moved in for financial reasons. Household income, offered as the mediator for women, mechanically includes the spouse's earnings, so adjusting for it partly adjusts for being married; the paper's own economies-of-scale theory would call for income per person. When the unmarried are broken out, never-married, divorced, and especially separated women still die at higher rates than married women with income held constant — only widows do not — so the "income explains it for women" finding is an average dominated by low-risk widows. The "immediate drop" at marriage is the value of a fitted line at zero years of marriage, comparing unmarried men to recently married men of the same age, not an observed change in anyone. The one claim that survives is the descriptive one: recorded marital status predicts death in this panel.

The paper announces a focus on protection at the outset and reasserts it in the closing sentence, while the paragraph immediately before that sentence concedes that people who drink, smoke, and stay out late are "probably precisely the people" who end up unmarried. Nothing that could have come out of these models would have counted against protection: an immediate drop reads as reduced risk-taking, a gradual one as accruing health benefits, and the paper offers both readings for the male result without choosing. Two of the three sex contrasts are described as significant or striking without a test and are not distinguishable from zero on the reported numbers; the third is a failure to detect a difference presented as a finding that contradicts the field. The pooled "income explains it for women" result and the disaggregated result showing it does not for three of the four unmarried groups both appear in the paper and are never reconciled. The abstract and the "his marriage / her marriage" passage state flatly what the body hedges. To the paper's credit, hypotheses are stated before results, anomalies are reported and labeled unexplained, and non-significant coefficients appear with their uncertainties, which is what makes these problems checkable.

For a 1995 sociology paper the reporting is reasonable: the data source is a public federal survey, the model is fully specified, funding is disclosed, hypotheses precede results, a reviewer's objection is quoted in a footnote, and the limitations paragraph is candid about the two problems that matter most. But the analytic file — augmented with decedent records and state death certificates — cannot be reconstructed, the custom estimation software is unavailable, and deaths are never reported by marital status, so a reader cannot check how many events underlie any contrast. Several results are "not shown," and the sex-difference claims are asserted without tests. The first results table, which carries the paper's opening set of claims, is illegible in the available copy.

The two citations that could be checked against full text, Goldman 1993 and Hu and Goldman 1990, are quoted and characterized accurately, and the framing literature is used at low stakes. Hu and Goldman 1990 report that marital-status mortality differences persist after socioeconomic controls, which conflicts with the paper's income finding for women, and they present cross-national evidence they read as selection; neither is mentioned. Helsing, Szklo and Comstock 1981, cited approvingly, found recently widowed men worse off than never-married men, while this paper finds them the same; the conflict is not addressed. The rejection of the social-integration hypothesis proceeds without citing the epidemiological literature that defines social integration through friendships and group ties rather than household composition (Berkman and Syme 1979; House, Landis and Umberson 1988). Goldman 1993, the paper's own chosen authority on selection, argues that inferences about protection are not justified from results like these.

Funding came from the National Institute on Aging, the authors are at RAND and the University of Chicago, and the data are a public survey. No party with a financial stake in the answer was involved. The only visible pressure is intellectual: the paper sets out to find a protective effect and concludes it found one, and the second author's later work developed this theme at length. That is a research program, not a conflict, and the findings are mixed enough (no larger benefit for men, the effect for women largely disappearing with income) that they do not read as engineered.