Mortality Differentials by Marital Status: An International Comparison

The design is adequate for descriptive questions: which unmarried group dies most, at what ages, and whether the recorded difference has changed. It cannot answer the causal question the abstract leads with. There are no controls beyond age and calendar period — no income, education, health behavior, or cause of death. Every death rate divides a count from one administrative system (death certificates, where a relative or clerk records marital status) by a count from another (censuses, where people self-report), and the paper never checks that the two agree, stating that it makes "no allowance for possible errors." The problem is worst for the smallest groups. Death rates here divide death-certificate counts by census counts — two systems that classify marital status independently. Someone widowed after the last census appears as "widowed" in the numerator but "married" in the denominator, making the widowed death rate look higher than it really is. This hits hardest for young widowed people, where the denominators are smallest and the paper's own proposed mechanism — shared accidents and infections killing both spouses in quick succession — is exactly the scenario that produces the mismatch. The design cannot tell the artifact apart from the real effect. Cells with fewer than 50 people were dropped, and the paper says this happened frequently for exactly this group of young widows; how many were dropped is not reported. For the group-size analysis, the census count of single people enters twice — as the population at risk and as the size measure — so any counting error produces a negative association with no selection involved. Five countries span under 20 years despite the claim about "two to three decades," and two have only three time points.

Poisson log-linear rate models with an exposure offset are the right tool for this data, and the internal arithmetic checks out. The problem is inference. The authors report their fullest model is rejected by the deviance test in 23 of 32 datasets and attribute this to enormous sample sizes, but residual deviance per degree of freedom is a direct estimate of overdispersion, and it runs from about 4 to 13. The reported t-statistics assume all variation in death counts is random (Poisson). The paper's own fit test shows it isn't — the real variation is 4 to 13 times larger. Adjusting for that would erase several of the starred results (Japanese men, Portuguese men, Danish men) and shrink the extreme values (t near 16 for divorced men in France and the USA) to something much less dramatic. Significance uses one-tailed tests at 5% even though the opposite sign appears and is discussed in several countries. The headline elasticity of −0.34 is averaged over the 28 negative coefficients only; over all 32 it is −0.27. No confidence intervals appear anywhere — not on the roughly 100 country-level ratios, the age-specific ratios (including off-scale values of 21.7, 28.8, and 58.7), or the trends. The two alternative fit measures are weak: 98% deviance reduction is dominated by age, and chi-square divided by exposure is near zero by construction for rare events. Trends for widowed and divorced groups are described in prose with specific percentages but no figures or coefficients.

The construct of interest is whether living with a spouse protects health and whether people who never marry are less healthy to start. The data measure legal marital status as recorded on two different documents. Cohabiting couples are "single"; separated couples are "married." The paper's own results show the proxy failing: the size effect vanishes in Denmark, Sweden, and Norway, which the authors attribute to informal cohabitation. The descriptive claims — men's excess larger than women's, divorced men worst — survive as descriptions of recorded categories. The selection claim does not. It asks aggregate ratios of administrative counts to reveal the health composition of a group, and no dataset here contains any measure of health. The association between group size and death rate is equally consistent with frailer members staying unmarried, with harsher conditions for members of rare groups (the authors' own alternative), with cohort differences in marriage timing, and with the counting artifact from using the same census figure twice. The paper treats cross-country consistency as evidence of a shared causal process. But all 16 countries build their rates the same way — ten draw from the same UN yearbook — so a shared measurement artifact would produce the same consistency. The countries most culturally distinct from Western Europe — Japan, Taiwan, and Scandinavia — are the exceptions on most patterns.

The descriptive findings are earned by the data. The interpretive layer is not. The paper opens by saying cross-sectional data cannot settle selection, closes by saying its findings "are not conclusive evidence for selection," and in between the abstract states that selection "is operating." The selection hypothesis and its stated rival, that rare-group members suffer stress and isolation, predict the same sign on the same coefficient, so the test cannot discriminate between them; calling the result "consistent with selection" is true but empty. The trend argument has the same shape: the paper lists the ratio's arithmetic as one of three possible explanations for the rise, notes that both groups' death rates fell in most countries, and then summarizes that "excess mortality has increased." The paper deserves credit for naming its exceptions rather than burying them, for excluding widowed people from the size analysis because widowhood and mortality cause each other, and for showing that period controls flip the sign of one coefficient. But the mechanical explanation for the core result — the census count entering twice — is never considered, and bereavement is dismissed as "hard to imagine" and replaced by a shared-risk story with no evidence in this dataset either.

The paper is candid about its interpretive limits: it says cross-sectional data cannot settle selection, that the ratio measure is hard to interpret and can rise while unmarried mortality improves, that young-widow cells are small, and that rarity stress is a rival to selection. Funding is disclosed and the models are written out in full, including a worked appendix. What is missing matters for checking the work. The assembled dataset is not provided, nor the list of dropped cells. No uncertainty is reported on any estimate. Trend results for two of the three unmarried groups are described in prose only. Counts are withheld where they would be informative — divorced women rank highest in "more than half" of countries, singles rose in "most." The headline size effect is averaged over the confirming cases only, disclosed in a way that requires the reader to redo the arithmetic. The abstract and conclusion disagree on the strength of the selection finding.

Nearly every core finding rests on the authors' own analysis of government data; the prior literature is scene-setting, and it is cited fairly. The paper cites a previous cross-country study — co-authored by the second author — that disagrees with the divorced-men ranking, and uses its own earlier work critically rather than as self-endorsement. The weaknesses are premises stated without citation. The introduction asserts that the married-unmarried difference survives correction for misreporting and persists after controlling for socioeconomic status; neither sentence carries a source, and this is the paper's only defense of making no allowance for data errors. The premise that never-married people are disproportionately unhealthy rests on one British cohort study. Cohabitation rates in Scandinavia are asserted without a source. The dismissal of bereavement leans on "mixed evidence" in four studies without saying what any of them found — one is a prospective study of 95,647 widowed persons built specifically to measure death after bereavement. A stronger argument was available (bereavement studies look at short-term excess risk, and even a doubling would not produce ratios above 10) and was not made.

Funding came from a single US federal grant; both authors were at a university demography unit. There is no commercial interest in the subject and the data are public. The only visible pressure is intellectual: the second author had already published the selection hypothesis (Kisker and Goldman 1987), and this paper is built to confirm it with a fuller model. That shows in three presentation choices — the headline average excludes the four contrary results, tests look only in the predicted direction, and the abstract drops the hedges the conclusion carries. Against that, contrary results are reported plainly, a rival explanation is offered and not ruled out, and the paper says up front that this kind of data cannot settle the question.