Case-Control Design

Case-Control Design, Odds Ratios and Use in Economic Models

A case-control study starts from people who already have the outcome of interest and asks how often they were exposed beforehand, compared with a sample of people from the same population who do not have the outcome. Because only a fraction of the non-cases is studied, the design can answer questions about rare or slow-developing outcomes, such as serious adverse drug reactions, with far fewer participants than following a whole cohort.

Why sampling on the outcome works

The STROBE explanation and elaboration paper describes case-control studies as comparing exposures between people with a particular disease outcome (cases) and people without it (controls), with the controls representing the cohort or population from which the cases arose. The case sample may be all or most of the available cases, while the control sample is usually only a small fraction of the people without the outcome. Labrecque and colleagues put the modern view plainly. A case-control study is an efficiently conducted cohort study, in which a subset of potential controls is sampled to measure the exposure distribution among them.

This view explains both the strength and the main demand of the design. The cases supply the numerator of an incidence comparison, and the controls stand in for the denominator, the people or person-time at risk in the source population. If the controls do not reflect the exposure distribution of that population, the comparison is distorted however many people are recruited.

The NICE real-world evidence framework (ECD9) states that case-control studies are most useful for rare outcomes or when further information on exposures must be collected, for example from manual medical record review or primary data collection. It also states that case-control studies conducted within existing database studies are generally not recommended, because they use less information than cohort studies. In health economics this places the design mainly in drug safety and aetiology questions about rare outcomes, where a cohort design would need very large numbers or long follow-up to observe enough events.

The odds ratio and what it estimates

A case-control analysis starts from a two-by-two table of exposure among cases and controls. The usual summary is the exposure odds ratio, the odds of exposure among cases divided by the odds of exposure among controls.

$$\widehat{OR} = \frac{a/b}{c/d} = \frac{ad}{bc}$$

where $a$ and $b$ are the exposed and unexposed cases, $c$ and $d$ are the exposed and unexposed controls, and $\widehat{OR}$ is the sample exposure odds ratio.

Labrecque and colleagues show that the same arithmetic estimates different population quantities depending on how the controls were sampled. Because the controls are a fraction $f$ of the relevant group, $f$ cancels from the ratio, which is why the design works without knowing $f$, and also why it cannot give absolute risks on its own.

Labrecque and colleagues stress that the case-cohort result is not an approximation but a mathematically equivalent way of expressing the risk ratio, show the same equality for the incidence rate ratio, and argue that each should be reported as such. The STROBE paper notes that the majority of published case-control studies sample open cohorts and so allow direct estimation of rate ratios. Only under cumulative sampling does the odds ratio need the rare-outcome condition to approximate a risk ratio, since odds and risk are close only when risk is small.

Nested case-control designs

A nested case-control study places case-control sampling inside an existing cohort or trial. Partlett and colleagues describe how each case is matched to a random subset of cohort members who have not yet had the outcome at that time; those controls may later become cases themselves and may serve as controls for other cases. This is incidence density sampling, so the estimate is a rate ratio.

The design was first used when data on an exposure were expensive or difficult to obtain for every cohort member, so only the cases and a random subset of controls were measured. Partlett and colleagues list three advantages over a conventional case-control study. Cases and controls come from the same population, exposures are measured before the outcome occurs, and cases can be matched to controls on time, such as age at the event. They also report that there is little statistical efficiency gained beyond four matched controls per case, with five controls only 4% more efficient than four, although more controls help when exposure among controls is uncommon (probability below 0.1). The case-cohort design is a related approach in which one random subcohort serves as the comparison group for every case.

Matching and analysis

Matching selects controls so that the distribution of chosen variables, often age and sex, is similar to the cases. The STROBE paper says that matching in case-control studies is done to increase efficiency. Pearce identifies two common misconceptions.

First, matching in a case-control study does not by itself control confounding by the matching factors and can even introduce it, so the matching factors must normally be adjusted for in the analysis. Second, he argues that a matched design does not always require a matched analysis; a standard stratified or unconditional logistic analysis that adjusts for the matching factors may be valid and can be more precise. A conditional analysis becomes necessary when matching is at or near the individual level, such as sibling controls, because sparse strata bias unconditional logistic regression. The STROBE paper adds that, in individually matched studies, a crude odds ratio that ignores the matching is usually biased towards one.

Selection bias, recall bias and confounding

The design is efficient because it works backwards from the outcome, and its main threats come from the same feature. The STROBE paper groups them into selection bias and information bias, and treats confounding separately.

• Selection bias arises when the probability of including cases or controls is associated with exposure. STROBE gives the example of deep-vein thrombosis being diagnosed more readily in women taking oral contraceptives. Hospital controls with other diseases can also mislead if the exposure affects the risk of developing, or being admitted for, those control conditions.
• Recall bias is the information bias that arises when cases recall past exposures more or less accurately than controls, or are more or less willing to report them. Interviewer bias can arise when interviewers know the hypothesis, so blinding helps. Exposure data recorded before the outcome occurred, as in many nested designs, do not depend on recall.
• Confounding produces associations that are real but not causal. Restriction, matching, stratification and multivariable adjustment address measured confounders; unmeasured ones remain, as with any observational study.

Using case-control estimates in economic models

A decision model needs absolute event probabilities, not only relative effects. The NICE framework (ECD9) lists designing, populating and validating economic models among the uses of real-world evidence, including baseline rates of events. A case-control estimate typically supplies the relative effect of an exposure, such as a drug on a rare adverse event, while the baseline risk comes from a separate population source such as a registry or cohort.

The Cochrane Handbook (chapter 15) makes the same point for converting an odds ratio into an absolute effect. An assumed comparator risk is required, and it is usually appropriate to repeat the calculation across a range of such risks. If the odds ratio is a disease odds ratio, the risk in the exposed group follows from the definition of odds, as below.

$$p_1 = \frac{OR \times p_0}{1 - p_0 + OR \times p_0}$$

where $p_0$ is the baseline (unexposed) risk over the model's time unit, $OR$ is the disease odds ratio and $p_1$ is the risk in the exposed group. If the study used incidence density sampling, the estimate is a rate ratio and is applied to a baseline rate before rate-to-probability conversion produces a transition probability for each model cycle. The study's population, exposure definition and follow-up period should also match the model's comparator, population and time unit. Either way, the uncertainty in the ratio and in the baseline risk should be carried into sensitivity analysis, and plausible bias in the ratio considered as a scenario.

Worked example of a rare adverse event in a cost model

All numbers in this example are illustrative. A case-control study of a serious liver reaction recruits 200 cases and 800 controls (four per case) sampled cumulatively from the same population; 40 cases and 80 controls had used the drug.

1. Odds ratio. Unexposed cases are 200 − 40 = 160 and unexposed controls are 800 − 80 = 720, so

$$\widehat{OR} = \frac{40 \times 720}{160 \times 80} = \frac{28800}{12800} = 2.25$$

where 40, 160, 80 and 720 are the cells $a$, $b$, $c$ and $d$ of the table. Cases make up 200 of the 1,000 people studied, but that 20% reflects the investigators' sampling, not the risk of the reaction.

2. Absolute risk. A registry gives an illustrative annual risk of 0.002 (2 per 1,000) in non-users. Then $p_1 = 2.25 \times 0.002 / (1 - 0.002 + 2.25 \times 0.002) = 0.0045 / 1.0025 = 0.004489$, a risk ratio of 0.004489 / 0.002 = 2.24, almost the same as the odds ratio because the event is rare.

3. Model inputs. The excess risk is 0.004489 − 0.002 = 0.002489, or 2.489 extra reactions per 1,000 patient-years of use. With an illustrative cost of GBP 6,000 and a QALY loss of 0.05 per reaction, the drug adds 2.489 × GBP 6,000 = GBP 14,934 and loses 2.489 × 0.05 = 0.124 QALYs per 1,000 patient-years.

4. When the outcome is common. With a baseline risk of 0.30, the same odds ratio gives $p_1 = 0.675 / (1 - 0.30 + 0.675) = 0.675 / 1.375 = 0.491$, a risk ratio of 1.64. Treating the odds ratio as a risk ratio (2.25 × 0.30 = 0.675) would overstate the exposed risk by 0.675 − 0.491 = 0.184.

5. Recall bias. If differential recall moved 10 unexposed cases into the exposed group (50 exposed, 150 unexposed), the odds ratio becomes (50 × 720)/(150 × 80) = 36,000/12,000 = 3.0. Then $p_1 = 0.006 / 1.004 = 0.005976$, and excess reactions rise from 2.489 to 3.976 per 1,000 patient-years, about 60% more, with costs and QALY losses rising in proportion.

Interpretation. The case-control study supplies the relative effect, and the model's absolute numbers depend on an external baseline risk. A modest recall error moves the safety cost substantially, which is why the bias scenario belongs in the model's sensitivity analysis.

Related designs and where each applies

A cohort design follows people from exposure to outcome and can measure risks directly; it is preferred when outcomes are common or when data on the whole cohort already exist. A cross-sectional study measures exposure and outcome at one time and has more difficulty establishing that exposure came first. The STROBE paper calls the case-crossover study one of the variants of the case-control design; in the example it quotes, each driver acts as their own control, which suits a brief exposure that transiently raises the risk of a rare outcome.

Where case-control evidence is misread

Labrecque and colleagues report that a 2008 review by Knol and colleagues of 150 case-control studies in 20 journals found that 90% reported only an odds ratio, even though most used designs that estimate risk ratios or incidence rate ratios. The label on the estimate therefore needs checking against the sampling scheme before it enters a model.

• The share of cases in the sample is set by design and is not a prevalence or risk.
• An odds ratio is not automatically a risk ratio; the difference grows as the outcome becomes common.
• Matching does not remove confounding by the matching factors.
• Associations from case-control studies are not causal effects without the usual assumptions about confounding, selection and measurement.
• Exposure must be shown to precede the outcome, which recall-based data cannot always guarantee.

Sources

• Labrecque JA, Hunink MMG, Ikram MA, Ikram MK. Do case-control studies always estimate odds ratios? American Journal of Epidemiology. 2021;190(2):318-321. https://doi.org/10.1093/aje/kwaa167
• National Institute for Health and Care Excellence. NICE real-world evidence framework (ECD9). Published 23 June 2022, last updated September 2025. https://www.nice.org.uk/corporate/ecd9
• Partlett C, Hall NJ, Leaf A, Juszczak E, Linsell L. Application of the matched nested case-control design to the secondary analysis of trial data. BMC Medical Research Methodology. 2020;20:117. https://doi.org/10.1186/s12874-020-01007-w
• Pearce N. Analysis of matched case-control studies. BMJ. 2016;352:i969. https://doi.org/10.1136/bmj.i969
• Schünemann HJ, Vist GE, Higgins JPT, et al. Chapter 15: Interpreting results and drawing conclusions. In: Higgins JPT, Thomas J, Chandler J, et al., editors. Cochrane Handbook for Systematic Reviews of Interventions, version 6.5. Cochrane; 2024. https://www.cochrane.org/authors/handbooks-and-manuals/handbook/current/chapter-15
• Vandenbroucke JP, von Elm E, Altman DG, et al. Strengthening the Reporting of Observational Studies in Epidemiology (STROBE): explanation and elaboration. PLoS Medicine. 2007;4(10):e297. https://doi.org/10.1371/journal.pmed.0040297