The Times They Are a Changin': Marital Status and Health Differentials from 1972 to 2003

The paper pools 32 annual rounds of a nationally representative survey, applies survey weights, and — improving on the one prior study (Waite 2000) — separates the widowed, divorced, separated, and never-married rather than lumping them. As a description of how reported-health differences moved, this is competent and the sample is enormous. But the design supports only description, and the paper's central conclusions are about what marriage does. Three problems are built into the data. Cohabiting couples are invisible for 25 of 32 years and sit in the never-married and formerly-married cells; since cohabitors report health like the married, the rise of cohabitation alone would push the never-married average toward the married — the paper's lead finding. Including only the household member who answered produces a sample two-thirds female, with married men drawn from whoever was home when the interviewer called — a subset whose makeup changed over the period and that carries the "married men stayed flat" result behind the gender conclusions. And the widowed, who show the largest decline, aged over the period while more disabled elderly people moved from institutions (excluded from the survey) into households; age is modeled as a straight line with no allowance for change across years. The limitations section is candid about selection into marriage but does not mention the respondent or cohabitation problems.

The ordered logistic regression with year × marital status interactions is an appropriate structure for a descriptive trend analysis, and the coefficients are interpreted correctly. Beyond that the analysis is thin. No standard errors or confidence intervals are reported — only coefficients to three decimals with significance stars, which at n = 1.1 million carry almost no information. The 32-year trend is forced to be linear in log-odds for every group with no test of nonlinearity, and figures show fitted lines rather than observed yearly proportions. The 1982 response-format change is absorbed by a single intercept shift, though the recode coefficient differs significantly by race (.333 vs .587) and by gender; a recode × marital status interaction was the obvious check and was not run. Age enters linearly; the age × widowed coefficient (.023) nearly cancels the main age slope (−.029), a sign the interaction is absorbing curvature at ages 70–80 where the widowed concentrate. The proportional-odds assumption is untested. The income "mediation" test compares coefficients across nested logit models, which rescale when a predictive covariate is added (Mood 2010); the data show exactly that — the married trend triples from .003 to .009 and every marital-status baseline flips sign — yet the paper calls this "little change." The one mediation claim it does make (income explains white convergence) rests on .003** becoming .001 n.s., with no test of the difference. The gender contrasts on divergence are slope differences of .005/year between a group starting at parity (women) and one starting with a penalty (men); by 2003 the implied penalties are nearly equal, which the discussion concedes but the abstract does not. Table 4 contains apparent typos (age for whites −.29; a sign flip on age × widowed) that do not affect conclusions but suggest the tables were not proofed.

The descriptive claims are sound as accounts of what respondents said. Every claim that reads those shifts as changes in what marriage does is stretched or disconnected. "Benefit of marriage" is operationalized as the difference between self-selected groups measured once each, with no transitions, no mechanism, and no duration in status. The never-married group is not the same group across the period: it absorbed a rising number of hidden cohabitors and shifted from older lifelong singles to young adults delaying marriage. "Married men" means married men who answered the survey. The claim that social change rather than income drives the trends rests on no variable for norms, stigma, or family structure — it is inference from what was not measured, after adjusting for one crudely measured variable (family income, with changing category boundaries and undisclosed handling of missing values). The policy conclusion asks a counterfactual — would the never-married be healthier if they married? — that snapshots of currently single people cannot answer. The "every race and gender group" claim about never-married improvement sums two estimates without testing the sum; for women and whites it is near zero.

The paper sets up two opposing predictions, convergence and divergence, and attributes both to social change. The results split, and the conclusion is that social change matters. Had the results been reversed, the same conclusion would have followed. The most obvious rival explanation for the lead finding — hidden cohabitors filling the never-married category — is never raised, though the paper's own sensitivity check supplies the fact that cohabitors look like the married. The income test is read two ways: "little change" when trends survive adjustment, "explained by income" when the white never-married trend loses significance after the same adjustment. The abstract frames the gender finding as dissolution hurting women more, when the data show women's penalty rising from about zero to match a penalty men already had; the discussion describes this accurately as the gender difference having diminished. Credit is due: hypotheses are stated in advance, the failed gender prediction is reported plainly, and the widowed divergence is called "unexpected" under the authors' own stress model rather than rationalized.

The data are a public federal survey, the questionnaire wording is quoted, funding is disclosed, and exclusions are counted. But the analysis is not reproducible from the paper: no code, no software named, no year-by-year or cell counts, and the same sample size reported with and without family income despite substantial missing income in this survey, with no word on how that was handled. The limitations section is substantive on selection, income measurement, and reporting drift, but omits the 65%-female sample, the invisible cohabitors, and the possibility that the 1982 format change affected marital groups differently.

Nothing checked was misrepresented, and the empirical results rest on the authors' own analysis rather than on any citation. The problems are selective emphasis. The paper calls the widowed decline "consistent with previous studies on mortality trends," citing a Dutch study ending in 1970, while the US-inclusive study it also cites (Hu and Goldman 1990) points to the divorced. Williams and Umberson 2004 — co-authored by one of the present authors, using longitudinal data from inside this study's window — found dissolution harmed men's self-rated health but not women's; the present paper concludes the opposite trend and never confronts it. No cited evidence on norm change after 1989 supports the claim that norms rather than income drive the trends. A working paper (Musick and Bumpass 2006) carries rhetorical weight in framing the policy debate.

Single federal grant, public data, no product or service at stake, no financial conflicts. The paper reports results contradicting its stated gender hypothesis and a co-author's own theoretical model, and says so plainly. The only visible pressure is intellectual: the closing policy paragraph echoes the sociological mainstream's skepticism of marriage promotion and goes beyond what the data can carry. The body of the paper, which reports that the married stayed healthiest throughout and that the formerly married are worse off than ever, does not.