PU520 Unit 8 Coffee Study Bias Seminar Reflection Example

I Blamed Smoking and the Room Blamed the Controls: A Seminar Reflection on the 1981 Hospital-Based Study Linking Coffee to Pancreatic Cancer, and How a Session on Bias and Confounding Moved My Explanation From a Confounder to the Choice of Comparison Group

[Student Name]

Purdue University Global

PU520: Principles of Epidemiology

Unit 8 Seminar Reflection

[Instructor Name]

[Date]

The seminar and classmates are composite and credited by position; the studies discussed are real.

The Study

In 1981, a research group reported a strong association between coffee drinking and pancreatic cancer in a case-control study of patients with pancreatic cancer and control patients hospitalized under the care of the same physicians. Relative risk rose with cups per day, reaching [2.7] for three or more cups, and the association was not affected by controlling for cigarette use (MacMahon et al., 1981). The finding drew wide attention. Later research did not confirm a meaningful link.

Where I Started

I reached first for smoking. Smokers drink more coffee, and smoking is an established cause of pancreatic cancer. If smoking were not fully controlled, coffee could appear harmful by riding along with it. Several classmates made the same argument, and it was a reasonable first move.

The Turn

The instructor asked us to reread the methods. The study had adjusted for smoking, and the association barely changed. Then the instructor asked: who were the controls? They were patients admitted by the same gastroenterologists, many for disorders of the digestive system, such as ulcers and other conditions that lead doctors to advise, or patients to choose, less coffee. If the controls drank less coffee than people in the population that produced the cases, the gap between groups would show up as a risk even if coffee caused nothing. The cases may not have drunk too much coffee; the controls may have drunk too little. That is selection bias, not confounding. Controls should reflect exposure in the population from which cases arose (Wacholder et al., 1992). A critique published the same year made this point, arguing that control selection and other features of hospital-based case-control designs could produce such a result (Feinstein et al., 1981).

How the Session Ran

The instructor began by asking us to vote on the most likely explanation before discussing anything. Most of us chose confounding by smoking; a few chose chance; nobody chose control selection. Then we read the methods paragraph aloud, one sentence at a time, and the instructor stopped us at the description of the controls. Seeing my own vote recorded on the board made the shift harder to ignore: I had chosen an explanation the paper had already tested, without reading carefully enough to notice.

What I Now Look for First

A checklist emerged from the session that I intend to keep: who the cases are and where they came from; who the controls are and whether they come from the same population; how exposure was measured and whether cases and controls might report it differently; which confounders were measured and adjusted; and only then, what the results show. Reading in that order puts design before findings, which is the habit this study taught.

Why the Difference Matters

If the problem were confounding, the fix would be better measurement and adjustment. Because the problem was likely in who was chosen as controls, no amount of statistical adjustment could repair it; only a different comparison group could. I had been reaching for a statistical answer to a design problem.

Where I Ended

I still think smoking deserved checking, and the authors checked it. But I now see control selection as the first question to ask of any hospital-based case-control study: would these controls have been exposed at the same rate as the population that produced the cases? In this study the answer was probably no, and in a direction that inflated the association.

What Classmates Added

One classmate pointed out that the study's dose-response pattern, usually a sign of causation, could also arise from biased controls if the controls' coffee reduction was strongest among those with the most serious digestive illness. Another noted that the study was carefully done for its time and that its authors called for confirmation, which the field then provided. Both points kept me from treating the study as a cautionary tale about careless researchers.

What I Will Do Differently

When I read a case-control study, I will write down who the controls are and how their exposure might differ from the source population before I look at the results. I will also ask whether the authors adjusted for the confounder I suspect, rather than assuming they did not.

A Question I Still Have

How should a researcher choose hospital controls at all, if almost every admitting diagnosis might be related to some exposure? Population controls avoid the problem but are harder to recruit and may answer questions differently.

References

Feinstein, A. R., Horwitz, R. I., Spitzer, W. O., & Battista, R. N. (1981). Coffee and pancreatic cancer: The problems of etiologic science and epidemiologic case-control research. JAMA, 246(9), 957-961. https://doi.org/10.1001/jama.1981.03320090019020

MacMahon, B., Yen, S., Trichopoulos, D., Warren, K., & Nardi, G. (1981). Coffee and cancer of the pancreas. New England Journal of Medicine, 304(11), 630-633. https://doi.org/10.1056/NEJM198103123041102

Wacholder, S., McLaughlin, J. K., Silverman, D. T., & Mandel, J. S. (1992). Selection of controls in case-control studies: I. Principles. American Journal of Epidemiology, 135(9), 1019-1028. https://doi.org/10.1093/oxfordjournals.aje.a116396