Marital Status, Marital Transitions, and Health: A Gendered Life Course Perspective

Following the same people over time and separating those who changed marital status from those who stayed in one is a real advance over the one-time snapshots that dominated this literature. Controlling for starting health in the transition models and checking that the two survey intervals give similar answers are sound choices. But the design cannot carry the conclusions built on it. The mechanism the paper names — "strain" — is never measured; no question about marital quality, caregiving, or distress appears anywhere, so strain is the label given to whichever direction a number moves. The transition groups are small, and the smallest one (men who were widowed, perhaps a dozen to three dozen people) supports the most complex statistical model and produces the "recently widowed men decline, then recover" result that anchors the crisis story. Age-specific figures are straight-line projections from a cluster of 30-to-50-year-olds out to 70 and 80, past the ages where anyone actually divorced or remarried. The comparison of long-term unmarried people to the married is a snapshot of health at the second interview, not a change over time, despite a figure note claiming otherwise. A third of the original sample was gone by 1994, 43% of them dead, and attrition by transition group is never reported — so the widowers who fared worst may simply be missing from the cell where the paper reports recovery. And because everyone started in 1986, a 70-year-old and a 30-year-old differ in birth year exactly as much as in age, which the paper acknowledges once and then ignores.

The modeling framework — ordered probit with baseline health as a covariate, clustered standard errors, survey weights — is appropriate for a five-point ordinal outcome with two observations per respondent, and the predicted-probability arithmetic checks out. The problems are in what was done with it. The continuity models use two-tailed tests while the transition models switch to one-tailed tests with no explanation, including for a divorce coefficient whose sign was opposite to the hypothesis; recomputed two-tailed, several key interactions sit at p ≈ .01–.03. At least 24 interaction terms appear in the final models, chosen because they were significant in unreported preliminary models, with no multiple-comparison correction. No confidence intervals are reported; the female × widowhood term has a standard error of 1.216, an interval spanning from large harm to large benefit, yet the paper reads it as "no effect on women." The age extrapolations are the most serious problem: divorced men average age 41 with SD 11, so the reported −32 pp at age 70 is 2.7 SD from the mean with at most one supporting observation; divorced women range 25–68, so the +28 pp at age 70 contradicts the paper's own footnote about plotting within the data. The Table 1 entry for married→widowed men (mean .020, SD .083) is internally inconsistent for a dummy variable and implies a cell closer to 12 than 34. The "age matters as much as gender" claim is never tested by any effect-size comparison or nested model. The footnote dismissing fixed-effects models as impossible with two waves is wrong; a first-difference model was feasible and would have been the natural robustness check.

The paper says "physical health" throughout, but the measure is one global self-rating that tracks mood as well as body. Someone who leaves a bad marriage and feels relieved will rate their health higher without any physical change — exactly the alternative the "relief from strain" interpretation would need to rule out and cannot. The two competing theories — marriage supplies resources, or breakup inflicts strain — are never operationalized: no resource is measured except income, which is deliberately dropped from the continuity comparison, and no strain is measured at all. When divorce improved self-rated health, against prediction, the improvement was reinterpreted as relief from the strain of a troubled marriage, itself unmeasured. "Life course stage" is theorized as role salience and accumulated stressors but measured as age in years, which in a single-cohort design is inseparable from birth year. Of the three core claims, the first two are stretched beyond what the design supports and the third — that age matters as much as gender — rests on a comparison that was never made and on age-specific numbers at ages the sample barely contains. Dichotomizing at excellent/very-good also makes percentage-point contrasts mechanically larger at older ages, because fewer older people are in the top two categories to begin with.

The paper deserves credit for reporting the results that went against it: divorce was associated with better health on average, widowhood with none, remarriage did not help older adults, and continually widowed younger men were worse off than married men when the theory said they shouldn't be. It is candid about small cells and about not knowing whether health changed before or after the transition. But the framing absorbs every outcome. A decline after widowhood is strain; an improvement three years later is recovery from strain; a lasting deficit among long-widowed men is "complete recovery may be slow or may not occur"; an improvement after divorce is relief from strain. Swap the signs and the discussion would need only light editing. The "men but not women" conclusion converts a null result on a few dozen women — with uncertainty wide enough to include substantial harm — into a positive finding that women are unaffected; the body text says "not significantly," the abstract says "not." The honeymoon effect is inferred from a null in a different model on a different subsample: first marriage was followed by a 20-point gain with no fading over three to five years, but because long-married men aren't healthier than never-married men in a separate snapshot comparison, the paper concludes the gain must fade later. Selection — healthy people staying never-married, unhealthy people staying divorced — explains the same pattern without a honeymoon. The one-tailed tests appear only in the models where the authors hoped to find effects.

Typical for sociology in 2004. The data are a public federal survey anyone can obtain, the funding source is disclosed, the software and prediction formulas are spelled out, and one worked calculation appears in a footnote. There is no pre-registration (the practice did not exist in the field), no code, and no conflict-of-interest statement (not required then). Several supporting analyses — the baseline cross-sectional models, the age-squared checks, the preliminary interaction searches that determined what appears in the final tables — are "not shown" or "available upon request." The paper never states how many people experienced each transition, so a reader cannot see that the age-specific headline figures rest on a handful of cases or none. The limitations section names three problems (no fine-grained timing, possible reverse causation, small cells for four-way interactions) but omits the ones that most affect the conclusions: attrition by group, unmeasured mechanisms, age-cohort confounding, extrapolation past the data, and the model-selection process.

The cited works are represented fairly as far as can be checked, and the paper is candid that its crisis-model evidence comes from mental-health studies, one of them cross-sectional. But the citations are almost entirely scene-setting; the core claims rest on the paper's own data. Two supporting mechanisms — spousal regulation of health behavior and older widowers' household-skill deficit — come from the same survey via the second author's earlier work, so they are not independent corroboration. One of those earlier papers (Umberson 1992) found that entering marriage changed health behavior little, which would have complicated the honeymoon story and goes unmentioned. Two motivating sentences ("recent research raises serious questions"; "researchers have recently begun to speculate") carry no citation. The standard references on health selection into marriage (Goldman 1993; Lillard and Panis 1996) are absent, as is the explicit case that marriage benefits are causal and durable (Waite 1995; Waite and Gallagher 2000), which is the position being argued against. And the paper opens by citing evidence that marital dissolution raises death rates, especially for men, then finds that divorce improves self-rated health for men under about 54 and women at every age, without addressing the tension.

No funding or affiliation conflict. The work was supported by a National Institute on Aging training grant, the data are a public survey the authors did not collect, and no commercial or advocacy party has a stake in the answer. The only visible pressure is the authors' advance commitment to the crisis model, which shows in interpretation rather than in how the data were produced: every ambiguous result is resolved toward the preferred theory, and the strongest single finding — a 20-point health gain after first marriage, a direct prediction of the rival theory — is relabeled a honeymoon effect. Reviewers from the opposing camp, including Linda Waite, are thanked for comments, and the analysis is reproducible from public data. Theoretical commitment is an ordinary academic pressure and does not by itself distort findings.