1Cohort studies are the strongest observational design for causal inference. They're also expensive, often slow, and hard to hold together over years of follow-up.

2Now let's flip the case-control logic on its head. Instead of starting with disease and looking backward to exposures, we start with exposures and follow people forward to see who develops disease. That's the cohort study: we identify a group of people who share some characteristic, or vary on an exposure of interest, and we follow them over time to see what happens.

3There are two main flavors of cohort studies. Prospective cohort studies define the cohort in the present and follow them into the future. We measure exposures now, then wait months or years to see who develops the outcome. Retrospective cohort studies, also called historical cohorts, use existing records to reconstruct what happened in the past. We identify a cohort and their exposures from historical data, then follow their outcomes through records up to the present.

4Retrospective cohorts are powerful tools in resource-limited settings, where waiting years for prospective data isn't feasible. A retrospective cohort study in KwaZulu-Natal, South Africa, examined treatment outcomes among people on antiretroviral therapy using medical records, tracking patients from ART initiation through their treatment. Virologic suppression rates fell below UNAIDS targets, and mortality remained substantial even among those on treatment. Those were real gaps between what the program intended and what patients experienced, and they might have stayed hidden without systematic cohort analysis.

5The advantage of the retrospective approach here is speed. Instead of launching a new cohort and waiting a decade, researchers could analyze ten years of outcomes in the time it took to extract and clean medical records. But the limitation is stark. They were constrained to whatever data clinicians had originally recorded. If a potential risk factor wasn't documented in patient files, it couldn't be studied, no matter how important it might be.

6Similarly, a ten-year retrospective cohort in Ethiopia examined opportunistic infections among 515 people starting antiretroviral therapy. Using hospital records, researchers could analyze a decade of disease progression without waiting a decade to conduct the study.

7So here's the fundamental trade-off. A prospective cohort takes years and is very expensive, but we control data quality. A retrospective cohort can be analyzed in weeks to months, but its quality depends on the records. We gain years of time, and we give up control over what gets measured and how accurately it's recorded.

8When they're feasible, cohort studies offer real advantages. Because we measure exposure before the outcome occurs, we establish the temporal sequence that case-control studies struggle with. We can calculate true incidence, because we have both numerators and denominators. We can study several outcomes from a single exposure: a cohort of smokers can examine lung cancer, heart disease, stroke, and COPD at once. And because exposures are measured in the present or from records, cohort studies are less vulnerable to recall bias. These advantages come at a cost in time and money, and a vulnerability that case-control studies sidestep.

9The central threat to cohort studies is loss to follow-up. People move, drop out, die of other causes, or simply stop participating. If loss to follow-up is related to both the exposure and the outcome, we've got a problem.

10Imagine we're following a cohort to study whether a new antiretroviral regimen reduces mortality compared to standard treatment. If people on the new regimen who start feeling sick are more likely to drop out and seek care elsewhere, we'll underestimate mortality in that group. The comparison is now biased, because we're missing precisely the people who matter most. The South Africa ART cohort faced this challenge, in a setting with high mobility and fragmented health systems.

11We can't know for certain what happened to the people we lost to follow-up. Maybe they died. Maybe they moved and are perfectly healthy. Maybe they switched to a different facility. Each possibility changes the interpretation. Researchers handle this with complete case analysis, with sensitivity analyses under best and worst cases, or with methods like multiple imputation and inverse probability weighting, and none of them is perfect. Those methods can help if we measured good predictors of dropout, but they can't help with predictors we didn't measure.

12Conventional guidance in clinical epidemiology often uses simple thresholds. Losses under 5% are typically considered unlikely to threaten validity, and losses over 20% raise serious concern. These heuristics are useful for quick appraisal, but they aren't sufficient. The critical issue is whether the loss introduces selection bias, whether the people lost differ from those retained in ways related to both exposure and outcome. Even small losses can bias estimates if missingness is informative, while larger losses may be less of a problem if they're random or handled appropriately in the analysis.

13Changes in exposure status are another challenge that's often overlooked. People start or stop smoking. Dietary patterns change with seasons or economic shocks. Medication adherence waxes and wanes, and bed net use varies across seasons. This is the problem of time-varying exposures, and it's everywhere in global health research. The classic approach, measuring exposure once at baseline, treats exposure as static when it's actually dynamic.

14Think of a cohort following physical activity and cardiovascular disease over 10 years. People's activity levels change a lot over a decade: they age, develop joint problems, have children, change jobs. If we only measure at baseline, we're asking whether physical activity at one moment predicts cardiovascular risk a decade later. That's a very different question from whether sustained physical activity reduces risk, which is probably what we care about.

15Measuring exposure repeatedly lets us account for those changes, but then we face time-varying confounding. If health status affects both the exposure and the outcome, and health status changes over time, standard adjustment methods don't work. Specialized methods like marginal structural models or g-estimation are beyond the scope of this chapter, but they're important to know exist.

16Cohort studies establish temporal sequence and calculate true incidence, and they're expensive, slow, and exposed to loss to follow-up. And confounding remains a threat. Knowing that exposure came before outcome doesn't mean other factors aren't driving the association. That's where we'll turn next.