Contents
On this page
- The defining structure of the case-control design
- Control sampling and the quantity estimated
- The rare disease assumption and why it is not required
- Functions and analytic implications of matching
- Sources of bias
- Indications for the case-control design
- Reporting a case-control study
- Key points
- Application to your study
- Frequently asked questions
Academy · Research Data Analytics & AI · Case-control studies
Case-Control Studies: Design, Control Sampling and the Interpretation of the Odds Ratio
A case-control study samples on outcome and examines prior exposure. Both the strengths and the vulnerabilities of the design follow from this inversion, in particular the fact that the method of control selection determines what the odds ratio estimates. The rare disease assumption, which many textbooks still present as a requirement, is not one.
The case-control design is appropriate when the outcome is rare and the exposure is not, a situation that applies to a large proportion of questions in clinical research. It is also the design most frequently conducted poorly, and the deficiency lies far more often in control selection than in the analysis. Two principles should be established at the outset: controls are not simply healthy individuals, and the odds ratio is not a single fixed quantity, since its interpretation depends on the sampling scheme by which controls were obtained. This article examines the structure, sampling, analysis and reporting of case-control studies.
Learning objectives
- The definition of a case-control study, and the advantages and costs of sampling on outcome
- How the three control sampling schemes differ and which measure each estimates
- Why the rare disease assumption is not required, and what replaces it
- The functions and limitations of matching, and the analytic obligation it creates
- How selection bias and recall bias arise, and which design features limit them
- The reporting items that a case-control study must address
Common misconceptions
- “Controls are healthy individuals.” Controls are individuals from the same source population as the cases who had not developed the outcome at the relevant time. They may have other conditions. The essential criterion is that they would have been identified as cases had they developed the outcome.
- “A case-control study requires the disease to be rare.” This is incorrect. The rare disease assumption is not required for case-control studies of common diseases; the control sampling scheme determines which measure is estimated, and with density or case-cohort sampling the odds ratio estimates a rate ratio or risk ratio directly.
- “Matching removes confounding.” Matching controls selection; it does not by itself remove confounding from the estimate, and it creates an obligation to analyse the data as matched. In simulations, unadjusted unconditional logistic regression underestimated the true exposure effect in every exact-matching scenario tested.
- “An odds ratio has the same meaning regardless of design.” Both the value computed and the quantity it estimates depend on the design. The same data analysed as though controls had been sampled differently address a different question.
- “Case-control studies are inherently low quality.” They are vulnerable in specific, identifiable ways. A case-control study with complete case ascertainment, controls from the same source population, exposure measured from records rather than recall, and a matched analysis can be methodologically strong; a study with volunteer controls and exposure assessed by interview cannot.
The defining structure of the case-control design
A case-control study identifies individuals who have the outcome of interest (the cases) and a comparison group who do not (the controls), and then compares their exposure histories retrospectively 17. Sampling is therefore on outcome, which inverts the cohort design.
The principal advantage is efficiency for rare outcomes. If an outcome occurs in a small number of individuals per thousand per year, a cohort study requires a very large population and prolonged follow-up to accumulate sufficient events, whereas a case-control study can identify events wherever they have already occurred and compare them with a modest number of controls. For many questions it is the only affordable design, and for some it is the only feasible one.
The principal cost is the denominator. The frequency of the outcome cannot be estimated, because the investigator determines how many cases and how many controls are included 19. For this reason the default measure is an odds ratio rather than a risk or rate ratio, and the quantity that the odds ratio estimates must be determined by reference to the design rather than assumed 28,29.
Two requirements define a defensible study. Cases must be ascertained in a manner that does not depend on exposure; if exposed individuals are more likely to be diagnosed, a spurious association is produced 20. In addition, controls must be drawn from the same source population as the cases, meaning that they would have been identified as cases had they developed the outcome 12,24. Our page on epidemiological designs compares this with the alternatives, and cohort studies covers the design it inverts.
Control sampling and the quantity estimated
This is the central concept of the article. The control sampling scheme determines which measure of effect the odds ratio estimates 26,29. Three schemes are standard, and they are not interchangeable.
Cumulative or exclusive sampling. Controls are selected from those who have not developed the outcome by the end of the risk period. The odds ratio estimates the odds ratio of disease, and only approximates a risk ratio when the outcome is uncommon — this is the scheme that gives rise to the rare disease assumption.
Density or risk-set sampling. Controls are selected from those still at risk at the time each case occurs, so a person may serve as a control for an early case and later become a case themselves. The odds ratio estimates a rate ratio directly, with no rarity requirement 26.
Case-cohort or inclusive sampling. Controls are a random sample of the whole cohort at baseline, including those who later become cases. The odds ratio estimates a risk ratio directly, again with no rarity requirement.
The practical consequence is that the scheme should be chosen according to the measure required, and the scheme used must then be reported. A paper reporting an odds ratio without describing control sampling has not reported its design, and readers cannot determine what the estimate means. This also explains why nested case-control studies within cohorts are usually density-sampled: the cohort provides the risk sets, and the resulting estimate is a rate ratio 22.
Control sampling schemes and the measure each one estimates
| Scheme | Controls are sampled from | The odds ratio estimates | Rare disease assumption needed? |
|---|---|---|---|
| Cumulative (exclusive) | Those still free of the outcome at the end of the risk period | The disease odds ratio; approximates a risk ratio only when the outcome is uncommon | Yes; the assumption applies to this scheme |
| Density (risk-set) | Those still at risk at the time each case occurs; a control may later become a case | A rate ratio, directly | No |
| Case-cohort (inclusive) | A random sample of the full cohort at baseline, including future cases | A risk ratio, directly | No |
The control sampling scheme, not the frequency of the outcome, determines which measure is estimated — which is why the rare disease assumption is not a requirement for case-control studies of common diseases. Nested case-control studies within cohorts are usually density-sampled, because the cohort supplies the risk sets.
The control selection sentence in a case-control paper
Scheme unidentifiable
Cases were patients diagnosed with the condition at the study hospital between 2018 and 2022. Controls were patients attending the same hospital during the study period without a diagnosis of the condition, matched to cases by age and sex. Exposure history was obtained by interview. Odds ratios were estimated using logistic regression adjusted for age, sex and smoking status.
Sampling scheme unidentifiable. “Patients attending the same hospital without the diagnosis” does not state when they were sampled relative to the cases, so a reader cannot determine what the odds ratio estimates.
Hospital controls from an undefined source population. They are ill, and if their illness shares risk factors with the outcome, the exposure contrast is suppressed.
Case ascertainment tied to one hospital. If referral to that hospital is related to exposure, the association is partly artefactual.
Interview-based exposure. Cases recall exposures differently from controls, and nothing in the description limits recall bias or blinds the interviewer.
Matched design analysed unconditionally. Unadjusted unconditional logistic regression underestimated the true effect in all six exact-matching scenarios in simulation; entering matching variables as covariates is not equivalent to conditioning.
No control-to-case ratio. Consequently, precision cannot be assessed and the sampling cannot be reconstructed.
Scheme identifiable
Cases were all residents of the defined catchment area with an incident, histologically confirmed diagnosis of the condition recorded in the regional registry between 1 January 2018 and 31 December 2022; ascertainment was through the registry rather than through the treating hospitals, so it does not depend on where or by whom a patient was investigated. For each case, three controls were selected by density sampling from the same catchment-area population register, drawn at random from those alive, resident and free of the condition on the date of that case’s diagnosis; a person selected as a control for an earlier case remained eligible to become a case later, and two did. Controls were matched to cases on sex and on year of birth within two years. Exposure was ascertained from dispensing records held independently of the registry, covering the whole catchment population, so neither recall nor interviewer knowledge of case status could influence it. Because controls were density-sampled, the resulting odds ratio estimates a rate ratio; no rare disease assumption is required. The analysis is conditional logistic regression on the matched sets, with the matching variables not entered as covariates, and with smoking status entered as a covariate because it was not matched on.
The sampling scheme is stated in a way that identifies it as density sampling, which fixes the interpretation of the odds ratio as a rate ratio.
The source population is a defined catchment with a population register, so controls demonstrably come from the population that generated the cases.
Ascertainment through a registry rather than through treating hospitals removes the dependence of case-finding on referral patterns.
Exposure is obtained from records held independently of case status, which removes recall bias and interviewer effects simultaneously.
Conditional logistic regression is used with the matching variables correctly excluded as covariates, matching the analysis to the design.
The detail that two controls later became cases confirms density sampling was genuinely implemented, rather than merely described.
Control selection determines whether a case-control study succeeds or fails, and the first version omits the one item of information a reader requires in order to interpret the result. The second allows a reader to identify the sampling scheme, the measure estimated and the bias mechanisms that have been addressed.
The rare disease assumption and why it is not required
The conventional textbook argument is that the odds ratio approximates the risk ratio when the disease is rare, and that case-control studies are therefore valid only for rare outcomes. The second part of that argument does not follow, and the claim has been addressed directly in the methodological literature: the rare disease assumption is not required for case-control studies of common diseases, because the control sampling scheme determines the measure estimated 26.
The reasoning is straightforward once the sampling schemes are distinguished. The rarity requirement applies to one specific scheme, cumulative sampling, in which the odds ratio is used as an approximation to another measure. Under density sampling the odds ratio estimates a rate ratio exactly, and under case-cohort sampling it estimates a risk ratio exactly. No approximation is involved, so no rarity condition is required.
This has practical importance because it considerably widens the legitimate range of the design. Case-control studies of common outcomes are entirely defensible provided that sampling is density or case-cohort and the analysis corresponds to the sampling. What is not defensible is cumulative sampling on a common outcome followed by interpretation of the odds ratio as a risk ratio, which is a real and frequent error that inflates effects away from the null.
Functions and analytic implications of matching
Matching selects controls to resemble cases on one or more variables — commonly age, sex, site or calendar time. Its purpose is to improve efficiency and to ensure overlap on strong confounders, so that the comparison is made within strata where both cases and controls exist.
Matching does not, however, remove confounding by itself 24. Matching builds the matching variable into the selection process, so that the crude comparison is distorted by the matching: controls have been made to resemble cases on that variable, and the unadjusted comparison no longer reflects the relationship in the population. The remedy is analytic, and the analysis must account for the matched structure.
The magnitude of the problem is measurable. In simulations of matched case-control data, unadjusted unconditional logistic regression underestimated the true exposure effect in every exact-matching scenario tested (six of six). In one scenario the estimate was 2.203 against a true value of 2.27 4. The attenuation is modest in that case, but it is systematic and in a known direction, and it is entirely avoidable: conditional logistic regression on the matched sets is the appropriate analysis 4. Our page on the statistical analysis of case-control studies examines the alternatives and the considerably larger errors that occur when the functional form of a matching variable is misspecified.
Two further cautions apply. The effect of a matched variable cannot be studied, because its variation between groups has been removed by design. Over-matching, that is, matching on a variable on the causal pathway between exposure and outcome, attenuates or eliminates the association under investigation 27.
Simulation of matched case-control data: unadjusted unconditional logistic regression underestimated the true exposure effect in every exact-matching scenario tested. The attenuation is modest in magnitude but systematic in direction, and it is avoided by conditioning on the matched sets.
Sources of bias
Three mechanisms account for most of the criticism directed at the design, and all three are problems of design rather than of analysis 16,27.
Selection bias in controls. Controls recruited by convenience (hospital visitors, volunteers, respondents to an advertisement) differ from the source population in ways that are frequently related to the exposure. Hospital controls present a particular risk: they are ill, and if their illness shares risk factors with the outcome under study, the difference in exposure between cases and controls is suppressed 25. The appropriate test is whether each control would have been identified as a case had the outcome developed.
Recall bias. When exposure is ascertained by questioning, individuals who have the outcome search their memory differently from those who do not 27. They have typically been asked about causes already, have read about the condition, and have reason to remember. The remedies are to use records rather than recall where possible, to use structured instruments administered identically to both groups, to blind interviewers to case status where feasible, and to prefer exposures that are documented rather than remembered.
Differential case ascertainment. If exposed individuals receive more medical attention, their cases are detected while unexposed cases are missed, which creates an association where none exists. For this reason, the route of ascertainment matters as much as the case definition.
None of these is a reason to avoid the design. They constitute a list of four or five requirements, and a study that satisfies them is not inherently weaker than other observational research.
Indications for the case-control design
The design is the appropriate choice in four situations.
A rare outcome. This is the classic indication. A cohort large enough to accumulate the events would be unaffordable, and the cases already exist.
A long induction period. If exposure precedes outcome by decades, prospective follow-up is impractical and historical exposure records are the only route.
Multiple exposures to examine. Because sampling is on outcome, a single case-control study can look at many candidate exposures at once, which suits early hypothesis generation — with the usual caution about multiplicity.
An expensive exposure measurement inside an existing cohort. The nested case-control design, where the expensive assay is performed only on cases and sampled controls 22. This is the setting in which the design is strongest, because the cohort supplies a defined source population and the risk sets for density sampling.
The design is inappropriate when absolute risk is required, when the exposure can be obtained only by questioning participants and the outcome is one about which people hold causal theories, or when several outcomes must be studied simultaneously; the last of these indicates a cohort or case-cohort design instead 18. See our study design support and biostatistics pages.
Reporting a case-control study
STROBE includes a case-control-specific checklist, and the most important items follow directly from the vulnerabilities of the design 9,10.
The case definition and the route of ascertainment should be given, together with a statement of whether ascertainment could have depended on exposure. The source population should be described, with an account of how controls were selected from it in sufficient detail for a reader to identify the sampling scheme as cumulative, density or case-cohort. The matching variables and the number of controls per case should be stated. The report should describe how exposure was measured, by whom, and whether the person collecting it was aware of case status. The numbers approached, eligible and participating should be reported separately for cases and controls, because differential participation is itself a mechanism of selection. Finally, the analysis model should be named; it should be conditional logistic regression if the design was matched.
The sentence most frequently absent from case-control papers is one describing control sampling with sufficient precision to identify the scheme 12,26. Without it, the odds ratio has no defined interpretation, however carefully it was computed. See the STROBE case-control checklist and the STROBE overview.
Key points
Key points
A case-control study samples on outcome and compares exposure histories retrospectively. Its efficiency for rare outcomes is well established, as is its dependence on two design decisions: case ascertainment that does not depend on exposure, and controls drawn from the same source population that generated the cases. The sampling scheme determines the measure: cumulative sampling yields a disease odds ratio that approximates a risk ratio only when the outcome is uncommon, density sampling yields a rate ratio directly, and case-cohort sampling yields a risk ratio directly; for this reason, the rare disease assumption is not a requirement for case-control studies of common diseases. Matching controls selection and creates an analytic obligation rather than fulfilling one: in simulations, unadjusted unconditional logistic regression underestimated the true exposure effect in all six exact-matching scenarios, yielding 2.203 against a true value of 2.27 in one. Conditional logistic regression should be applied to the matched sets, and the sampling scheme should be reported with sufficient precision for a reader to identify it.
Application to your study
Application to your study
- The source population should be defined before any controls are selected. Each potential control should then be assessed against the criterion of whether the individual would have been identified as a case had the outcome developed.
- The sampling scheme should be selected according to the measure required. Density sampling is appropriate for a rate ratio and case-cohort sampling for a risk ratio; cumulative sampling is appropriate only if the outcome is genuinely uncommon.
- Cases should be ascertained by a route independent of exposure. A registry or complete population source is preferable to a single treating centre, because referral patterns may themselves be related to exposure.
- Recorded exposure is preferable to recalled exposure. Dispensing, laboratory or administrative records held independently of case status eliminate both recall bias and interviewer effects.
- Matching should be used sparingly and never on variables on the causal pathway. Over-matching attenuates the association under study, and the effect of a matching variable cannot be estimated.
- Matched data should be analysed conditionally. Conditional logistic regression should be applied to the matched sets, without the matching variables as covariates.
- The numbers approached, eligible and participating should be reported separately for cases and controls. Differential participation is a mechanism of selection bias and cannot be detected without these numbers.
- The sampling scheme should be identified explicitly in the report. Without this information, the odds ratio has no defined interpretation, however carefully it was computed.
Frequently asked questions
A study that identifies individuals who have the outcome of interest, assembles a comparison group who do not, and compares their prior exposure. Sampling is on outcome, which inverts the cohort design and makes the study efficient for rare outcomes: rather than following a large population forward and awaiting events, the investigator identifies events where they have already occurred. The cost of that inversion is the denominator; because the investigator determines how many cases and controls are included, the frequency of the outcome cannot be estimated. The default measure of association is therefore an odds ratio, and what that odds ratio estimates depends on how the controls were sampled.
No. The rare disease assumption is not required for case-control studies of common diseases, because the control sampling scheme determines which measure is estimated. The rarity condition applies to one specific scheme: cumulative sampling, in which controls are drawn from those still free of the outcome at the end of the risk period and the odds ratio is used as an approximation to a risk ratio. Under density sampling, where controls are drawn from those at risk at the time each case occurs, the odds ratio estimates a rate ratio exactly. Under case-cohort sampling, where controls are a random sample of the baseline cohort, it estimates a risk ratio exactly. No approximation is involved, and therefore no rarity condition applies.
Controls should be drawn from the same source population that generated the cases, using a defined scheme, with the selection documented sufficiently for a reader to identify the scheme. The operational test for an individual control is whether that person would have been identified as a case had they developed the outcome; if not, the individual belongs to a different population and the comparison is confounded by whatever distinguishes the two. Convenience sources, such as hospital visitors, volunteers and respondents to advertisements, usually fail this test. Hospital controls present a particular hazard, because they are ill, and if their illness shares risk factors with the outcome being studied, the exposure contrast is suppressed toward the null.
No. Matching controls the selection of controls so that cases and controls overlap on strong confounders, which improves efficiency and ensures comparable strata. However, it builds the matching variable into the selection process, which distorts the crude comparison and creates an obligation to analyse the data as matched. The evidence on the consequences of failing to do so is specific: in simulations of matched case-control data, unadjusted unconditional logistic regression underestimated the true exposure effect in every exact-matching scenario tested (six of six), including an estimate of 2.203 against a true value of 2.27. Conditional logistic regression on the matched sets is the appropriate analysis, with the matching variables not entered as covariates.
Principally by not relying on recall. Where exposure can be obtained from records held independently of case status (dispensing data, laboratory results, occupational records, administrative databases), recall bias does not arise, and this is the strongest available design feature. Where interview is unavoidable, an identical structured instrument should be used for both groups, administered where feasible by an interviewer unaware of case status, with questions anchored to verifiable events rather than open recall. Documented exposures should be preferred to remembered ones, and the discussion should state explicitly the direction in which recall is likely to have operated, since cases have usually already been asked about causes by their clinicians.
Yes, and this is one of the practical advantages of the design: because sampling is on outcome, a single study can examine many candidate exposures at once, which suits early hypothesis generation. The usual caveats about multiplicity apply, since testing many exposures without pre-specification will produce associations by chance, together with a design-specific caveat: the quality of exposure measurement usually differs between exposures, so a study with an excellent record source for one exposure and interview recall for another should not present them as equally reliable. A single case-control study cannot examine more than one outcome, because the sampling is defined by the outcome; that requires a cohort or case-cohort design.
A nested case-control study is conducted within a defined cohort, with controls sampled from that cohort. The practical advantage is that the source population problem is solved by construction: the cohort defines who was at risk, so controls demonstrably come from the population that generated the cases, and the cohort supplies the risk sets for density sampling. It also makes expensive exposure measurement affordable, since the assay is performed only on cases and sampled controls rather than on the whole cohort. The ordinary design must establish its source population by argument rather than by construction, and this is the source of most of its vulnerability.
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Pubrica Academy. “Case-Control Studies: Design, Control Sampling and the Interpretation of the Odds Ratio.” Pubrica. October 9, 2026. https://pubrica.com/academy/concepts-definitions/what-are-case-control-studies/
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Pubrica Academy. Case-Control Studies: Design, Control Sampling and the Interpretation of the Odds Ratio. [Internet]. Pubrica; 2026 Oct 9 [cited 2026 Oct 15]. Available from: https://pubrica.com/academy/concepts-definitions/what-are-case-control-studies/
Pubrica Academy, “Case-Control Studies: Design, Control Sampling and the Interpretation of the Odds Ratio,” Pubrica, Oct. 9, 2026. [Online]. Available: https://pubrica.com/academy/concepts-definitions/what-are-case-control-studies/
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author = {{Pubrica Academy}},
title = {Case-Control Studies: Design, Control Sampling and the Interpretation of the Odds Ratio},
howpublished = {Pubrica},
year = {2026},
month = {oct},
url = {https://pubrica.com/academy/concepts-definitions/what-are-case-control-studies/},
note = {Accessed: <span data-cite-acc="iso">2026-10-15</span>}
}This article is written to be learned from. Cite it if you are referring to what it says; if you are using the evidence behind it, cite the sources listed above instead.
Case-control design specification
This should be completed before any control is selected. The choice of sampling scheme determines what the result will mean, and it cannot be made retrospectively.
CASE-CONTROL STUDY DESIGN SPECIFICATION
1. THE QUESTION
Outcome: ___________________________________________________
Exposure(s): _______________________________________________
Measure of effect wanted: [ ] rate ratio [ ] risk ratio
[ ] disease odds ratio
2. SOURCE POPULATION
Defined as: ________________________________________________
Is there a population register or complete registry? [ ] yes
Source: __________________________________________________
[ ] no - how will the source population be established:
__________________________________________________________
3. CASES
Case definition: ___________________________________________
Confirmation method: ______________________________________
Incident or prevalent: [ ] incident [ ] prevalent
Ascertainment route: ______________________________________
[ ] Ascertainment does NOT depend on exposure status
If it might, how: _____________________________________
Period of case accrual: ___________________________________
4. CONTROLS - SAMPLING SCHEME (this fixes your measure)
[ ] Density / risk-set -> odds ratio estimates a RATE RATIO
Sampled from those at risk on the date of each case's
event. Can a control later become a case? [ ] yes
[ ] Case-cohort / inclusive -> estimates a RISK RATIO
Random sample of the baseline cohort, including future cases
[ ] Cumulative / exclusive -> disease ODDS RATIO only
Justify, and confirm the outcome is uncommon: __________
Controls per case: ______ (2-4 is usually sufficient)
Selection source: _________________________________________
[ ] Every control would have been captured as a case had they
developed the outcome
5. MATCHING
Matched on: _______________________________________________
Tolerance for each variable: ______________________________
[ ] Nothing matched on lies on the causal pathway
[ ] We are NOT trying to estimate the effect of a matched
variable
Analysis model: [ ] conditional logistic regression
[ ] unmatched - unconditional, adjusted
[ ] Matching variables NOT entered as covariates in the
conditional model
6. EXPOSURE ASCERTAINMENT
Source: [ ] records independent of case status
[ ] interview [ ] questionnaire [ ] mixed
If interview or questionnaire:
[ ] identical instrument for cases and controls
[ ] collector blinded to case status
[ ] questions anchored to verifiable events
Expected direction of recall bias: _______________________
Period of exposure window relative to the outcome: ________
7. CONFOUNDERS
Identified: _______________________________________________
Measured for both groups by the same method? [ ] yes
Handling: [ ] matched [ ] adjusted [ ] stratified
Likely direction of residual confounding: _________________
8. PARTICIPATION (report separately for cases and controls)
Cases: approached ____ eligible ____ participated ____
Controls: approached ____ eligible ____ participated ____
Differential participation and its likely effect: _________
9. REPORTING
[ ] STROBE case-control checklist mapped
[ ] One sentence identifies the sampling scheme explicitly
[ ] Measure the odds ratio estimates is stated
[ ] Analysis model matches the design Pubrica AcademyWritten and maintained by Pubrica’s subject matter experts. Articles are revised when the underlying standards change, and each article states the date on which it was last reviewed.
How Pubrica can help
Pubrica specifies case-control studies by first determining the measure required, a rate ratio or a risk ratio, from which the control sampling scheme follows. This reverses the usual order and addresses the principal reason why many published case-control studies cannot state what their odds ratio estimates. The team drafts the control selection paragraph so that a reader can identify the scheme, verifies that the analysis model matches the design, and identifies exposure sources that eliminate recall bias rather than merely acknowledging it.