Case-control studies: starting from the outcome
Chapter 12: Observational Designs — Video 3
https://ghrbook.com/videos/case-control-studies/

[Slide 1] Case-control studies start with the outcome and look back at exposures. They're the design of choice for rare diseases and outbreak investigations.
[Slide 2] Say we want to understand what caused a cholera outbreak in Yemen, a country experiencing active conflict, where prospective research is nearly impossible. We could wait months to set up a cohort study. Or we could work backward: find people who have cholera, find similar people who don't, and ask both groups about their recent exposures.
[Slide 3] That's the logic of a case-control study. We select cases, people with the disease or outcome of interest, and controls, people without it, ideally drawn from the same source population. Then we measure past exposures in both groups and compare. The question is whether cases were more likely than controls to have been exposed.
[Slide 4] In Yemen, researchers investigating cholera identified specific risk factors, like not washing khat before chewing it, and use of common-source water. This was a matched case-control study conducted in an active conflict zone, about as challenging a research environment as there is. By carefully matching controls to cases on geographic and demographic variables, the researchers generated actionable findings about how cholera was spreading.
[Slide 5] Case-control studies shine when the outcome is rare, because we'd need enormous cohorts to capture enough cases. They shine when we need answers quickly, when the outcome has already occurred, which makes them ideal for outbreaks, and when several exposures might matter, because we can assess many risk factors at once. But they introduce some distinctive challenges.
[Slide 6] The hardest part of a case-control study is choosing controls. Controls should represent the source population that gave rise to the cases. The test is a question: if a control had developed the disease, would they have been identified as a case? Get this wrong and we introduce selection bias, one of the most pernicious threats to case-control studies.
[Slide 7] Here's a classic mistake. We're studying risk factors for hospitalized pneumonia. We select pneumonia patients as cases, and other hospitalized patients, say surgery patients, as controls. The problem is that hospitalized patients aren't representative of the population that produced the pneumonia cases. If we're studying smoking, and smoking also increases the risk of surgery, we'll underestimate smoking's effect on pneumonia. Controls should come from the same population the cases came from, which often means community controls.
[Slide 8] Matching means selecting controls to be similar to cases on certain variables, like age, sex, or neighborhood. The Yemen study matched on geographic and demographic factors, which in a conflict zone meant cases and controls faced similar water infrastructure, sanitation, and access to services. We match to control confounding. But matching has a cost. If we match on age, we can no longer study whether age affects cholera risk. That information is locked away by design. Matching can be done pair by pair, or on the overall distribution, and individual matching requires conditional logistic regression.
[Slide 9] There's also a temptation to over-match, to match on too many variables or, worse, on variables that are consequences of the exposure. Imagine we're studying whether smoking causes lung cancer, and we match on chronic cough, which smoking causes. Smokers with chronic cough get matched to non-smokers with chronic cough. But non-smokers with chronic cough probably have other lung problems that might also increase cancer risk. We've made smokers and non-smokers artificially similar on unmeasured lung disease, and the apparent association between smoking and cancer shrinks.
[Slide 10] So here's the rule: never match on anything in the causal pathway between exposure and outcome. Matching variables should be confounders, common causes of exposure and outcome, and not mediators or colliders. If we're uncertain, we can draw a DAG. Matching on a variable strongly correlated with the exposure causes the same damage, and pushes the apparent effect toward the null.
[Slide 11] And if we match, we must account for it in the analysis, using conditional logistic regression or a similar method. Reviews of published case-control studies show this is often done wrong. Matched design, unmatched analysis is a recipe for bias. The pairs are linked by design, standard logistic regression assumes every observation is independent, and the result is wrong standard errors, wrong p-values, and misleading confidence intervals.
[Slide 12] Because case-control studies ask people to remember past exposures, they're vulnerable to recall bias. People with a disease might search their memories more intensely than healthy controls. Did you eat unwashed vegetables before you got sick? If you have cholera, you might remember every questionable salad. If you don't, you might shrug and say, probably. That differential recall can create spurious associations.
[Slide 13] One strategy is to use objective exposure measures when possible, like medical records, employment records, or environmental measurements. But in many global health settings, especially during emergencies, those records don't exist, and you work with what you have. Case-control studies also face information bias when exposure assessment differs between cases and controls. If interviewers know who has the disease, they might probe harder with cases, which is why blinding interviewers to case status is good practice.
[Slide 14] A hybrid design is worth knowing about: the nested case-control study. It starts with a cohort. When cases occur, we select controls from within the same cohort, people who haven't developed the outcome yet, and measure exposures, often from stored biospecimens, for cases and controls only. That keeps costs manageable when exposure assessment requires specialized lab tests. Exposures were measured before disease occurred, which eliminates recall bias and tells us exposure preceded outcome. The key requirement is an existing cohort with stored samples or detailed baseline data.
[Slide 15] Case-control studies are efficient, fast, and well suited to rare outcomes and outbreaks. But they can't calculate incidence or absolute risk, because we started with cases and not with a population at risk. And control selection is difficult and easily biased. Getting it wrong can invalidate the entire study.