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POSTPONING DEATH |
Institute for Health, Health Care Policy and Aging Research, Rutgers, The State University of New Jersey, New Brunswick, NJ 08901, and, Yale School of Medicine, Department of Epidemiology and Public Health, New Haven, CT 06520-8034
We are mystified by the appearance in Psychosomatic Medicine of a critique by Smith (1) of one part of our 1992 paper, "Religion, Disability, Depression, and the Timing of Death."(2) The publication of this critique takes place 11 years after the appearance of our article in the American Journal of Sociology, the leading and longest-published journal of sociology in the English language. The long reaction time means that readers are unlikely to have the original article fresh in their minds, as would be the case had the critique appeared in the ordinary way, in the same journal shortly after the paper was published. We invite the readers of Psychosomatic Medicine to read the original article, in which the distribution of deaths around religious holidays was only one of several health endpoints studied in a large representative sample of elderly persons in New Haven, Connecticut.
Even the full acceptance of Smith’s two main arguments—that we incorrectly used one-tailed rather than two-tailed z-tests, and were in error in our use of the continuity correction—would, at most, slightly weaken a small handful of the findings of our article, rather than change the general conclusions in any fundamental way. Indeed, Smith is correct when he says that the binomial distribution (rather than the normalized z score with continuity correction) should have been used in the case he cites—but this applies only to four (of 96) tests in which (the number of deaths around the holiday) multiplied by (probability of the event, which is .5) is less than or equal to 5. In other words, we should have used the binomial distribution in the four subgroup instances in our tables 3 and 4 in which the number of deaths before and after the holiday was 10 or fewer. In the other 92 cases, n was greater than 10, and thus the z-score was appropriate.
Smith’s characterization of our use of the continuity correction is not correct. We were not testing whether there were "3 or more" or "more than 3" deaths after the holiday—we were testing whether there were fewer deaths before the holiday, and thus we added the .5, the appropriate procedure for the continuity correction (3). Even so, in tables 1 and 2, with Smith’s "corrected" p values, only 6 of 96 tests change their p value from p < .05 to p > .05, and these changes are of less than dramatic magnitude (for example, p < .039 changes to p < .065).
The debate over one-tailed versus two-tailed tests is as old as the ages. Smith’s criticism of our use of a one-tailed z-test is based on the assumption that the one-tailed test is less conservative, and he implies that we "loaded the dice." The title, "A Cautionary Lesson" implies that other researchers should be cautious so they are not "discovered" as we have purportedly been. In fact, because we prevented ourselves from obtaining a significant finding regarding the very interesting phenomenon of more deaths of Jewish women before the Jewish holidays, one might say we were being more conservative, not less. Every Type I error is increased or decreased at the cost or benefit of its Type II error.
The only explicit reasoning given behind Smith’s argument in favor of a two-tailed test is his citation of the "lifeline" vs "deadline" findings in an article by Phillips et al. (4). In this article, there were more deaths among men before their birthdays (compared with after), and significantly fewer deaths among women. Although the Phillips et al.(4) findings illustrate that anniversary days can have impact on health outcomes over the short-term, a conclusion that Smith seems not to accept, its findings are not relevant to our 1992 article. For one thing, it focuses on birthdays, not on religious holidays. More subtly, as our data show, it is the meaning of the day, ie, whether it is a Christian or Jewish holiday, and whether the respondent is a devout or a nominal Christian or Jew, that matters, not the mere occurrence of the holiday. A minor issue of course, is that the article by Phillips et al.(4) appeared in the same year (1992) as ours and we could not have been aware of it while preparing our manuscript. Thus, we were testing the only hypothesis that could be derived from the extant literature at the time, and the one-tailed test was entirely appropriate.
The argument that the deaths may not be independent is characterized imprecisely and also incorrect. Smith’s example of harsher weather after Christmas is an argument for a spurious cause (not lack of independence of events) that would result in a larger number of deaths after the holiday. This argument has no merit for two reasons. First, our inclusion of the early spring holidays of Easter and Passover, when the weather is improving, neatly balances the fall/early winter holidays of Yom Kippur and Christmas. More importantly, if there were a seasonal effect it would have an equal impact on both Christians and Jews, and our data clearly show effects of holiday timing only for the relevant religious group.
Smith’s critique might be taken more seriously were it not for the fact that our finding on the timing of deaths around holidays was neither the first nor the last to be published. The first evidence of a "death-dip" before a religious holiday was in a classic article by Phillips and Feldman in 1973 (5). Other articles before ours concerning deaths around religious holidays appeared in 1988 (6) and 1990 (7). Our data, which included self-reported religious affiliations of the respondents and their usual level of attendance at religious services, represented more detailed measurement of individual-level data than had existed in the literature previously. Other studies (8, 9) that have appeared since 1992 have made further improvements in methods, design and sampling. This is the normal progress of science, for earlier studies to be surpassed by later ones. Smith’s critique might be more relevant to our appraisal of the holiday effect if it were applied to and resulted in nontrivial changes in the outcomes of all or at least a majority of these studies, as all of them report the same pattern: with rare exceptions, deaths occur less frequently before religious holidays than after. In the absence of that larger critique, what is the relevance of a minor criticism of one study that found the same pattern of deaths as all the others?
Given the improvements in conceptualization and method over the years in which this finding has been replicated, we can be assured that the holiday effect is stable, especially if studies focus on health outcomes for individuals for whom the holidays are emotionally significant. We expect that the editors and readers of Psychosomatic Medicine will draw their own conclusions on the meaningfulness and empirical soundness of this research and will recognize that our 1992 publication represented one of several small but significant steps that contribute to our understanding of this phenomenon.
The authors would like to acknowledge the advice and assistance of Howard Leventhal and Louise Russell.
NOTES
The authors of this letter were invited to reply to Gary Smith’s "Idler and Kasi p Values: A Cautiionary Lessan," which appears in this issue.
REFERENCES
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