PU570 Unit 3 Study Design Critique Example

One Case in a Hundred Thousand, Forty Years After the Exposure: A Unit 3 Study Design Critique Explaining Why a Registry-Based Case-Control Study Was the Only Sensible Design for Pleural Mesothelioma, and Where It Still Goes Wrong

[Student Name]

Purdue University Global

PU570: Chronic Disease Epidemiology

Unit 3 Study Design Critique

[Instructor Name]

[Date]

The registry study and its figures are composite; the disease's epidemiology, the design problems and the research cited are real.

The Study Being Critiqued

A composite state cancer registry identified 412 incident cases of pleural mesothelioma over fifteen years. Controls were 1,236 adults sampled from the same registry's colorectal cancer cases, matched three to one on age, sex and year of diagnosis. Occupational history was collected by telephone interview with the participant or, for 183 cases who had died, with a next of kin. The exposure of interest was any occupational asbestos contact, with a job-exposure matrix applied to reported job titles.

Why a Cohort Study Was Not Available

Three features of the disease rule it out. Incidence is roughly one per 100,000 per year, so a cohort of 100,000 adults followed ten years would be expected to produce about ten cases, which cannot support exposure-response analysis. The latency between exposure and diagnosis runs twenty to fifty years, so a cohort assembled today measures an exposure that mostly stopped decades ago. And the exposure is historical: the workplaces are closed and the dust is gone, so prospective measurement is impossible even in principle. For a rare disease with long latency, the case-control design is not a compromise but the correct choice (Robinson & Lake, 2005).

Why a Registry Was the Right Sampling Frame

Case ascertainment is the strength. A population-based registry captures nearly all diagnosed cases in a defined area, which removes the referral bias that would arise from recruiting at one or two specialist centers, where this disease concentrates. The registry also supplies diagnosis dates, which is what allows matching on calendar year, and that matters because diagnostic criteria for this tumor changed over the study period.

Problem One: The Controls Are Cancer Patients

Using another cancer's cases as controls buys cooperation and comparability of ascertainment, and it costs the study its claim to represent the source population's exposure distribution. Controls should represent the exposure experience of the population from which cases arose, and a second cancer is a population selected by its own risk factors (Wacholder et al., 1992). Colorectal cancer is associated with occupational sedentariness and with socioeconomic position, so the control group's job history is not the state's job history. If anything this biases the odds ratio toward one, since controls drawn from manual occupations would carry more asbestos exposure than the general population. The study's controls were chosen because they could be found and interviewed, which is the commonest reason for a control group and the weakest.

Problem Two: Exposure by Recall, Half of It Secondhand

Occupational history reported forty years later is imprecise for everybody and differently imprecise for cases. A person told they have a tumor linked to asbestos searches their memory for asbestos, and so does the widow answering for a husband who died. Next of kin supplied the history for 183 of 412 cases and for none of the controls, which is not a small asymmetry: proxies report job titles tolerably and exposures within a job poorly. The job-exposure matrix partly rescues this by assigning exposure from the title rather than from the participant's belief, and that is the study's best methodological decision.

Problem Three: Latency Is Not Handled

The analysis treats any occupational asbestos contact as the exposure, with no lag applied. For a disease with twenty to fifty year latency, exposure in the ten years before diagnosis cannot have caused the tumor, and including it dilutes the association. The standard correction, excluding exposure in a lag window before diagnosis, is cheap and was not done. This is the one criticism in the critique that the authors could remedy with the data they already hold.

Problem Four: Survivor Structure in the Case Series

Median survival is under a year, so the cases interviewed in person differ systematically from those represented by proxies, and both differ from the cases who died before the registry's interview attempt. The study reports no comparison between interviewed and proxy cases on age, job history completeness or stage, and that comparison is the minimum evidence a reader needs in order to judge the problem.

The Matching Decision, Weighed Separately

Matching three controls to each case on age, sex and year of diagnosis deserves its own paragraph, because matching is often treated as automatically good. Here it buys two things. Age matching removes a strong confounder that would otherwise dominate, since both this tumor and the comparison cancer rise steeply with age. Year matching handles the diagnostic drift mentioned above. What matching costs is also real: the matched variables can no longer be studied, so this design cannot examine whether the association differs by age, which is a question with implications for latency. Matching three to one rather than one to one adds precision with diminishing returns past about four controls per case, and at 412 cases the study was right to buy controls rather than to stop at equal numbers. The analysis, however, reports an unmatched odds ratio alongside a conditional one without explaining why they differ, and in a matched design the conditional estimate is the one that respects the sampling.

What the Study Establishes Anyway

The critique's conclusion is not that the study is uninformative. Within its design, the finding of a strong association with occupational exposure, with odds ratios rising across job-exposure matrix categories, is consistent with a body of evidence in which the exposure-response relationship is one of the clearest in occupational cancer epidemiology. A critique has to weigh what the biases could plausibly do against the size of the association, and an odds ratio of this magnitude is not produced by control selection and proxy recall alone (Rothman & Greenland, 2005).

Four Things the Authors Should Do Before Publishing

1. Apply a lag window and report the analysis both ways.

2. Compare interviewed and proxy cases on every available characteristic, and report the odds ratio separately for each.

3. Replace or supplement the control group with population controls from a sampling frame, even at a lower response rate, and report both.

4. State in the abstract that controls were cancer patients, which affects how every reader should interpret the figure, rather than leaving it to the methods section.

References

Robinson, B. W. S., & Lake, R. A. (2005). Advances in malignant mesothelioma. The New England Journal of Medicine, 353(15), 1591-1603. https://doi.org/10.1056/NEJMra050152

Rothman, K. J., & Greenland, S. (2005). Causation and causal inference in epidemiology. American Journal of Public Health, 95(S1), S144-S150. https://doi.org/10.2105/AJPH.2004.059204

Wacholder, S., Silverman, D. T., McLaughlin, J. K., & Mandel, J. S. (1992). Selection of controls in case-control studies. II. Types of controls. American Journal of Epidemiology, 135(9), 1029-1041. https://doi.org/10.1093/oxfordjournals.aje.a116397