Study designs: cross-sectional, cohort and case-control

• Observational studies are the backbone of population research: about nine of ten research papers published in clinical speciality journals describe observational research.^[1]
• The three main observational designs are the cohort study, the case-control study and the cross-sectional study.^[1] They differ in the order in which people are selected and in how time is used.
• A cohort study starts with exposure status, waits for (or looks back for) disease, and can measure incidence and relative risk.
• A case-control study starts with outcome status, looks backwards at exposure, and is the efficient choice for rare outcomes.
• A cross-sectional study takes a single snapshot of a population and is the natural design for measuring prevalence.
• Reporting standards exist for all of them: the STROBE checklist (22 items, 18 common to all three designs, 4 design-specific) is the reporting guide for observational studies.^[1]

By the end of this page you should be able to:

1. Define cohort, case-control and cross-sectional studies, and tell the three apart from the way participants are sampled.
2. Write down the formulas for prevalence, cumulative incidence, incidence rate, relative risk (risk ratio) and odds ratio, and explain what the null value (1) means.
3. Give the strengths and weaknesses of each design and state when each is the right choice.
4. Distinguish a prospective from a retrospective (historical) cohort study, and explain why the terms are best avoided.
5. Recognise nested designs (nested case-control and case-cohort) and say what they add.
6. Apply the STROBE, CONSORT, Cochrane Handbook vocabulary when you read or report a study, and avoid the common design pitfalls.

A study design is the plan that decides who enters a study, what is measured, in what order, and how time is used. Observational studies do not allocate exposure: they record what has already happened or is happening, then compare groups. Experimental studies (randomised trials) allocate exposure deliberately. STROBE provides general reporting recommendations for the three main observational designs that this page covers: cohort, case-control and cross-sectional studies.^[1]

Cohort study. The investigators follow people over time. They obtain information about people and their exposures at baseline, let time pass, then assess the occurrence of outcomes. Contrasts are made between exposed and unexposed people (or between different exposure categories). Several outcomes can be examined, and variables can be measured repeatedly during follow-up.^[1] A closed cohort enrols a defined group at the start (for example, a birth cohort) and follows them to a fixed end date. An open (dynamic) cohort has people entering and leaving at different times (for example, the inhabitants of a town); such cohorts can change because of births, deaths and migration while remaining roughly stable in composition over short periods.^[1]

Case-control study. The investigators compare exposures between people with a particular disease outcome (cases) and people without that outcome (controls). Cases and controls are sampled so that they represent an underlying cohort or a cross-section of a population, defined geographically or as the catchment of health services. Controls represent the population from which the cases arose. The odds of exposure are compared between cases and controls.^[1] In most modern case-control studies the design samples an open cohort, allowing direct estimation of rate ratios.^[1]

Cross-sectional study. The investigators assess all individuals in a sample at the same point in time, often to examine the prevalence of exposures, risk factors or disease. Some cross-sectional studies are analytical and estimate associations between exposure and disease by comparing disease prevalence between exposure groups, or by comparing odds of exposure between people with and without disease.^[1]

Other names you will meet. Follow-up study and longitudinal study are often used as synonyms for cohort study, and prevalence study as a synonym for cross-sectional study. STROBE warns that terminology is often used incorrectly or imprecisely, so a study should be classified by what was actually done, not by its title.^[1] STROBE recommendations do not specifically address other designs such as genetic linkage studies, infectious disease modelling, or case reports and case series.^[1]

Observational studies serve purposes from generating a first hint of a cause through verifying the magnitude of associations, and they are used creatively with existing data.^[1]

• Cohort studies are used when the research question is incidence or prognosis: what happens next to exposed people, how risk accumulates over time, and what adverse effects appear after years.
• Case-control studies are used when the outcome is rare, when latency is long, or when a quick, relatively cheap answer is needed (for example, in an outbreak).
• Cross-sectional studies are used when the question is "how common is this now?" and for surveillance, health services planning and screening programme design.

The mechanism of an observational study is inference from groups. Error enters in predictable ways, and naming them is the equivalent of knowing the pathophysiology of a disease.

• Confounding. A factor associated with both exposure and outcome distorts the apparent association. Confounding makes relations that are factually right but cannot be interpreted causally unless adjusted for.^[1]
• Selection bias. The way participants enter or remain in the study is related to exposure. In case-control studies, selection bias arises if the probability of including cases or controls depends on exposure.^[1]
• Information bias. Systematic differences in completeness or accuracy of data lead to misclassification. Examples include detection (surveillance) bias, recall bias and interviewer bias.^[1]
• Temporality. An association is not evidence that exposure preceded disease; this problem is clearest in cross-sectional studies, because exposure and outcome are measured at the same time.^[1]
• Random error. A deviation caused by statistical fluctuation, not by systematic error, and present in every design.^[1]

Bias usually arises during design or implementation and cannot be remedied later, so it must be addressed in the plan of the study and described in the report.^[1]

A useful habit is to read a methods and results section the way you would take a history and examine a patient.

• Who. Eligibility criteria, source population and method of recruitment. Detail about follow-up tells you whether loss to follow-up differed between groups.^[1]
• What was measured. Definitions of outcomes, exposures, predictors, potential confounders and effect modifiers, plus diagnostic criteria for any disease outcome.^[1]
• How it was measured. Sources of data, methods of assessment and their validity or reliability. If groups were not assessed the same way, information bias becomes likely.^[1]
• Bias plan. What was done to reduce potential selection bias, information bias and confounding, including matching strategy and number of controls per case in matched designs.^[1]
• Design label. Key elements of study design should appear early in the paper (title or abstract if STROBE is followed), so you can classify it yourself rather than trusting the authors' term.^[1]

The measure chosen must match the design. A design that cannot produce a measure should not be forced to.

Prevalence. The number of people who have a disease at a particular time, divided by the population examined at that time. It is a proportion (point prevalence at one moment, period prevalence over an interval). Prevalence is the natural output of cross-sectional studies and is used for surveillance, service planning and screening.^[1]

Incidence. The number of people who develop a disease over a defined period. It may be expressed as cumulative incidence, the proportion of people developing disease starting from an at-risk population (a risk, used with closed cohorts), or as incidence rate, cases per unit of person-time (used with open cohorts and dynamic populations).^[1]

Relative risk (risk ratio). The ratio of the incidence of the event of interest between exposed and unexposed groups. It is a ratio of cumulative incidences (or, in shorter form, rate ratios from incidence rates).^[1]

Odds ratio. The ratio of the odds of exposure among cases to the odds of exposure among controls. In a case-control study this is the primary measure, and depending on sampling it is interpreted as a risk ratio, rate ratio or (prevalence) odds ratio. The majority of published case-control studies sample open cohorts and so allow direct estimation of rate ratios.^[1]

A note on terms from systematic-review methodology: odds ratio, risk ratio, rate ratio and hazard ratio are all ratio measures of effect, and for all of them the value 1 represents no difference between groups, 0 is the lowest possible value and infinity the highest. Confidence intervals express the uncertainty around each estimate.^[3]

Attributable measures can move a result from relative to absolute terms: how much disease could be prevented by removing the exposure. Results may be more useful when expressed both in relative and absolute terms.^[1] For smoking, one estimate attributed 91% of lung cancers, 40% of coronary heart disease and 33% of all deaths among men in 2000.^[1]

Let a = exposed with outcome, b = exposed without outcome, c = unexposed with outcome, d = unexposed without outcome.

• Prevalence (point) = (all with disease at that time) / (population examined at that time).
• Cumulative incidence in exposed = a / (a + b).
• Cumulative incidence in unexposed = c / (c + d).
• Risk ratio = [a / (a + b)] / [c / (c + d)].
• Odds in exposed = a / b; odds in unexposed = c / d; odds ratio = (a / b) / (c / d) = ad / bc.
• Incidence rate = new cases / person-time at risk.

In a study of male British doctors, the incidence rate of death from lung cancer over 50 years of follow-up was 249 per 100,000 per year among smokers and 17 per 100,000 per year among non-smokers, a rate ratio of 14.6 (249 divided by 17).^[1]

• A ratio of 1 is the null value: no association between exposure and outcome on that scale.^[3]
• The further from 1, the larger the association, but magnitude must be read with the confidence interval and with absolute differences.
• Odds ratios are often mistaken for risk ratios. The assumption that odds ratio equals risk ratio holds only when the outcome is rare in both groups.
• Cross-sectional (prevalence) odds ratios describe co-occurrence, not incidence, and cannot by themselves show that exposure preceded disease.
• Relative measures without absolute context can exaggerate importance; presenting both is preferred.^[1]

The labels prospective and retrospective (sometimes concurrent and historical) are best avoided, because they are ill defined. Three different usages exist: cohort and prospective used as synonyms with retrospective for case-control studies; prospective versus retrospective cohort depending on whether data collection preceded or followed the idea for the study; and prospective versus retrospective case-control depending on whether exposure data existed when cases were selected. Some authors advise against the terms altogether and favour describing exactly how and when data collection took place.^[1]

In everyday usage:

• A prospective cohort is assembled now and followed forward: exposure and baseline data are collected today, outcomes are recorded later.
• A retrospective (historical) cohort uses data that already exist (records, registries) to define a cohort in the past and its outcomes up to the present.

The risk of retrospective data is not inferiority by default; it is that measurement, completeness and loss to follow-up were not under the investigator's control. The essential requirement is the same for both: describe exactly how and when data collection took place and whether it was the same for all groups.^[1]

Nested designs borrow strength from a parent cohort or population while saving cost. They are common in modern epidemiology and many STROBE items apply unchanged.

There is no clinical test for a study design, but there are conventional questions that separate one design from another. Treat them as a checklist, not as a score.

• Was exposure measured first and then outcome? If yes, the design is (or can be) a cohort study.
• Were participants sampled by outcome status? If yes, the design is case-control.
• Were exposure and outcome measured at one point in time? If yes, the design is cross-sectional.
• Is there a formal control group defined by a protocol? If yes, a case series has become a case-control study and a trial becomes worth checking for randomisation.
• Is randomisation present? If yes, the study is experimental, not observational, and CONSORT 2025 rather than STROBE is the appropriate reporting checklist.

For observational studies, the reporting checklist STROBE has 22 items in total, of which 18 are common to all three designs and 4 are design-specific.^[1] That 18-and-4 split is the only numeric threshold used routinely in this topic.

There are no drug doses in choosing a study design; "treatment" here means following the reporting and review standards that keep observational evidence readable. Name and use the editions actually applied:

• STROBE (2007, Explanation and Elaboration): the reporting checklist for cohort, case-control and cross-sectional studies; 22 items overall.^[1]
• CONSORT (first published 1996, updated 2001, 2010 and now 2025): the corresponding reporting checklist for randomised trials; use it as the contrast that shows observational designs are not trials.^[2]
• Cochrane Handbook (version 6.5, 2024): for how study designs are grouped and used in systematic reviews, and for the choice of measures of effect; the relevant chapters are 3 and 6.^[3]
• WHO public-health guidance, CDC field epidemiology training resources and NCBI Bookshelf (StatPearls): widely used teaching sources for these designs in public-health and clinical research training; use their current editions and check the version in force locally.

When two guidelines differ (for example, when a journal requests STROBE but a thesis committee requests a local checklist), the honest response is to say that reporting standards differ by institution and to meet the stricter of the two.

The complications of a weak design are the biases above, and they are complications in the clinical sense: preventable if anticipated, costly if missed.

• Selection bias after the fact produces spurious or missed associations and cannot be removed by analysis.
• Information bias misclassifies exposure or outcome, usually biasing estimates toward the null (for example, non-differential misclassification of a binary exposure).
• Confounding by indication is a particular risk when treatment or behaviour is chosen because of risk.
• Small or distorted control groups in case-control studies, including overmatching, can make odds ratios unusable.
• Loss to follow-up in a cohort study can silently change who remains in the at-risk population.
• Survivor or prevalence-incidence bias in cross-sectional studies can make a fatal disease look rare and a long-lasting condition look common.
• Publication and optimism bias are higher when the design does not pre-register or cannot control allocation, and they are one reason trials and reviews exist alongside observational work.

A study's value over time depends on its transportability. Cohort and case-control studies are often less directly transportable than trials because the exposure was not controlled, but they are the only designs that can study exposures that cannot ethically be randomised.

• Describe setting, locations, eligibility, recruitment and the completeness of follow-up so readers can judge generalisability.^[1]
• Relative measures without absolute measures overstate impact; present both when the design allows.^[1]
• Absolute differences and population-attributable fractions convert association into public-health terms.^[1]
• A null value of 1 is a null value of association only on the measure's scale; it still has to be checked against the confidence interval.

Prevention and screening are built on prevalence and incidence data, so the designs map cleanly onto them.

• Cross-sectional studies measure the burden of disease or of a risk factor at one time, which guides whether a screening programme is worth piloting.
• Cohort studies provide incidence, so that the absolute benefit of prevention can be quantified.
• Case-control studies work well for evaluating screening effectiveness when the outcome (advanced disease) is rare and the screening exposure is binary.
• Open cohorts estimate incidence rates and rate ratios; closed cohorts estimate cumulative incidences (risks) and risk ratios.^[1]

Quoting the population perspective: global attributable estimates of smoking (91% of lung cancers, 40% of coronary heart disease and 33% of all deaths among men in 2000) show how a risk factor's absolute burden can be expressed even where experiments are impossible.^[1]

Pregnancy, children and older adults are studied with the same three designs, but the sampling problems are sharper.

• Pregnancy. Registries, birth cohorts and nested case-control studies using stored antenatal samples are common; confounding by gestational age and indication matters, and follow-up often splits by pregnancy outcome.
• Children. Birth cohorts and repeated cross-sectional surveys dominate; because events are rare, nested designs are efficient. Be careful about interpreting associations as causation when exposure and outcome are measured together in childhood surveys.
• Older adults. Open cohorts and repeated cross-sections are typical, but competing risks, attrition and multimorbidity need explicit handling.
• Subgroup analyses. There is a strong tendency to look for evidence of subgroup-specific associations, particularly when overall results suggest little or no effect. Subgroup claims need prespecified hypotheses, adequate sample size and appropriate tests for interaction.^[1]
• A recurring trap of case-control work in these groups is overmatching: matching cases and controls on variables close to the exposure can remove the information you are trying to study and lower power. Matching is not always appropriate and should be justified factor by factor.^[1]

• Calling a count an incidence. A single snapshot gives prevalence; incidence needs measurement over time.
• Calling a study "prospective" without defining it. Describe when and how data were collected, and for whom.^[1]
• Odds ratio is not risk ratio unless the outcome is rare.
• Cross-sectional associations are not proof that exposure caused the outcome. Temporality is not established.
• Control selection is the most common failure of case-control studies; controls must represent the source population from which cases arose.
• Overmatching can destroy the information in a case-control study.
• Matching is not always appropriate or necessary. Factor-by-factor justification and a matched or stratified analysis are required when used.^[1]
• Mislabelling study design in the title or abstract leads to incorrect indexing; STROBE item 1 asks for a commonly used term.^[1]
• Reading the p-value instead of the design: a precise, biased estimate is less useful than an imprecise unbiased one.

• The three main observational designs are cohort, case-control and cross-sectional, and much published research is observational.^[1]
• Cohort: exposure first, then time, then outcome; incidence and risk (rate) ratios are measurable; good for multiple outcomes and uncommon exposures.
• Case-control: outcome first, then exposure; efficient for rare outcomes and long latency; odds ratio is the main measure.
• Cross-sectional: one point in time; prevalence and current association; weak for causation and temporality.
• Closed cohorts estimate cumulative incidence (risk) and risk ratios; open cohorts estimate incidence rates and rate ratios.^[1]
• A case-control odds ratio is, depending on sampling, a risk ratio, rate ratio or (prevalence) odds ratio; most case-control studies sample open cohorts and estimate rate ratios.^[1]
• 1 is the null value for risk ratio, rate ratio, odds ratio and hazard ratio, with confidence intervals measuring uncertainty.^[3]
• Relative measures should be paired with absolute measures; both together inform action.
• Retrospective and prospective are ill-defined labels; define when and how data were collected instead.^[1]
• Nested designs (nested case-control, case-cohort) reuse a parent cohort efficiently, especially for rare outcomes or stored samples.
• Reporting standards by study type: STROBE (22 items, 18 common, 4 design-specific) for observational studies; CONSORT 2025 for trials; Cochrane Handbook version 6.5 for systematic reviews.^[1][2][3]
• Bias enters at design and cannot be repaired later; report selection, information and confounding with magnitude and direction.
• Temporality is the central weakness of cross-sectional designs and a common problem even in other designs.

• Public-health epidemiology: prevalence, incidence, mortality and disease burden.
• Systematic reviews and meta-analysis (Cochrane; choice of effect measures).
• Diagnostic and screening test evaluation (sensitivity and specificity).
• Bias and confounding in observational research.
• Listening to the news: appraising a research abstract.