Free scoping read. A written assessment of your manuscript in two business days, at no cost.

Start one
Contents

Academy · Research Data Analytics & AI · Epidemiology designs

Epidemiological Designs for Clinical Trials: Cohort, Case-Control and Nested Designs in Trial Programmes

A randomised trial answers one question well: the effect of assigning a given intervention. Almost every other question that a trial programme must address — eligibility, the untreated course of the condition, the attributability of a rare harm, and outcomes after the follow-up window closes — is an epidemiological question requiring an epidemiological design. The ability to match each design to the question it answers is therefore a core competence of trialists.

Pubrica AcademyWritten by the medical writing and biostatistics teams Reviewed byPubrica biostatistics team Published9 October 2026 Last checked9 October 2026 Reading time12 minutes Sources30 peer-reviewed

Trial teams frequently regard observational designs as the option used when randomisation is not possible. That framing produces substantive errors, because these designs are not weaker versions of a trial; they answer different questions and fail in different ways. A nested case-control study, for example, exists because measuring exposure is expensive: in one published example, exposure was measured in 74 cases and 147 controls drawn from a parent cohort of 25,802 — under 1% of the cohort — to answer a question that the whole cohort could not afford to answer. Such a design is a reasoned methodological choice rather than a compromise.

Learning objectives

  • The epidemiological designs that answer each question around a trial programme, and the measure of effect each yields
  • The rationale for the nested case-control design and its costs relative to analysis of the whole cohort
  • The application of cohort principles — person-time, competing risks and loss to follow-up — within a randomised trial
  • A precise statement of what randomisation does and does not protect against
  • The circumstances in which an external or historical comparison is defensible
  • The reporting guideline applicable to each design, and why applying the trial guideline constitutes a category error

Common misconceptions

  • “Observational designs are what you use when randomisation is impossible.” They are appropriate when the question does not concern assignment. Natural history, eligibility, exposure-outcome attribution in rare harms and long-term outcomes after a trial closes are all questions that a randomised comparison cannot answer at any sample size.
  • “A case-control study is a cheap cohort study.” It is a distinct design with a different sampling logic. It samples on outcome rather than exposure, which is why it estimates an odds ratio by default and why control selection determines the meaning of the estimate.
  • “A nested case-control study is a weaker version of analysing the full cohort.” It is a deliberate efficiency: the expensive exposure is measured in all cases and in a sample of the cohort. In the published example, 74 cases and 147 controls from a parent cohort of 25,802 provided an answer that measuring 25,802 exposures would not have been funded to provide.
  • “Randomisation handles confounding, so a trial needs no epidemiological thinking.” Randomisation balances confounders in expectation at baseline. It does not address differential loss to follow-up, competing risks, post-randomisation selection, or the difference between the trial population and the population that will receive the treatment.
  • “Long follow-up is a matter of keeping the trial open.” Extended follow-up rapidly becomes a cohort study attached to a trial and acquires the problems of cohort studies: non-random attrition, outcomes ascertained by means different from those used during the trial, and comparisons that are no longer protected by the original randomisation.

The role of epidemiological designs in a trial programme

Four questions arise in every trial programme and none of them is answerable by the randomised comparison.

Who is eligible, and how many of them are there. A feasibility estimate is a descriptive epidemiological question about a defined population. An inaccurate estimate is the most common cause of a trial that fails to recruit.

What happens without the intervention. The control arm indicates what happens under trial conditions, with trial-level monitoring, in a consented population. Sample size estimation, interpretation and any external comparison require the natural history of the condition in the population being treated, which is the domain of cohort studies.

Whether a rare harm is attributable. No trial is powered for events occurring at a rate of a few per thousand. Attribution for rare harms is established through case-control and cohort designs in much larger populations, usually after the trial programme ends 17,18. Our pages on case-control studies and periodic safety reporting cover that handover.

What happens after the trial window. Extended follow-up of a randomised cohort is an epidemiological study with a randomised origin, and the protection that randomisation offers diminishes as attrition accumulates.

The designs described below are therefore not alternatives to the trial. They complement it, and the trial is one instrument in a programme that requires several.

Available designs and the measures of effect they yield

Six designs cover most of the requirements of a trial programme, and the distinguishing question is always the basis on which participants were sampled.

Cohort study. Participants are sampled on exposure and followed forward to the outcome. The design yields incidence, risk and rate ratios. It can be prospective, retrospective or ambidirectional — the direction describes when the data were collected relative to the start of the study, not the direction of the logic, which is always from exposure to outcome 18. The term derives from the Roman military unit, a body of 300 to 600 men, ten of which made a legion; the sense of a defined group moving together through time is apt 18.

Case-control study. Participants are sampled on outcome, and exposure is ascertained retrospectively. The design yields an odds ratio, and what that odds ratio estimates depends on how controls were sampled 17,26.

Nested case-control study. A case-control study conducted inside a defined cohort, with controls sampled from the cohort. Yields an odds ratio that, with appropriate control sampling, estimates a rate ratio 22,26.

Case-cohort study. Cases plus a random subcohort sampled at baseline, which allows direct estimation of rates and permits several outcomes to be studied against one subcohort.

Cross-sectional study. Sampling is on neither exposure nor outcome; both are measured at once. The design yields prevalence and cannot establish temporal order.

Before-and-after or interrupted time series. Sampling is on time. The design is useful for service-level changes but vulnerable to secular trends unless the series is long enough to model them.

Each design has its own reporting guideline branch — see STROBE for cohort studies, STROBE for case-control and STROBE for cross-sectional.

Design, sampling basis and estimable measures

DesignWhat you sample onMeasure it yieldsApplication in a trial programme
CohortExposure; follow forward to outcomeIncidence, risk ratio, rate ratioNatural history, eligibility frames, long-term outcomes after a trial closes
Case-controlOutcome; look back to exposureOdds ratio — what it estimates depends on control samplingRare harms, attribution questions no trial is powered for
Nested case-controlOutcome within a defined cohort; controls sampled from the cohortOdds ratio that can estimate a rate ratio with appropriate samplingExpensive exposures or biomarkers in a trial biobank
Case-cohortAll cases plus a random subcohort from baselineRates directly; one subcohort serves several outcomesSeveral outcome questions against one stored sample set
Cross-sectionalNeither — both measured at oncePrevalence; no temporal orderFeasibility, burden of disease, instrument performance
Before-and-after or interrupted time seriesTimeLevel and slope changeService-level or pathway changes where randomisation is not available

Design definitions as conventionally stated in the epidemiological literature. Cohort studies may be prospective, retrospective or ambidirectional; the direction refers to when data were collected relative to the study’s start, not to the logic, which always runs from exposure to outcome.

Rationale for the nested case-control design

This is the design of greatest relevance to trial programmes, because it addresses a problem that trials frequently encounter: an exposure or biomarker that is expensive to measure and an outcome that is uncommon.

The logic is straightforward. A cohort with stored samples or retrievable records is available. All cases that occurred are identified. A set of controls is sampled from the same cohort. The expensive exposure is then measured only in those individuals. In the published example, a nested case-control study analysed 74 cases and 147 controls drawn from a parent cohort of 25,802 recruited from 1974 — which means exposure was measured in under 1% of the parent cohort 18,21,22.

The gain is the ability to address the question at all. The cost is precision, which is governed by the number of cases rather than by the size of the cohort: 74 cases remain 74 cases whether the cohort was 25,802 or 250,000. The usual control-to-case ratio of two or three, as in the 147-to-74 example, reflects the fact that adding controls beyond about four per case yields very little further precision.

For a trial programme with a biobank, this is the design that converts stored samples into an answer. The practical requirements are that the cohort be well defined, that case ascertainment be complete, and that controls be sampled from those still at risk at the time each case occurred — the detail that determines whether the odds ratio estimates a rate ratio 12,24,26. Our page on the statistical analysis of case-control studies covers the matched analysis this implies.

25,802people in the parent cohort, recruited from 1974
74cases in which exposure was measured
147controls sampled from the cohort
under 1%of the parent cohort had exposure measured

A published nested case-control study, showing why the design exists: exposure was assessed in 221 people rather than in 25,802, which is what made an expensive measurement affordable. Precision is set by the 74 cases, not by the size of the parent cohort.

Cohort principles within a randomised trial

A randomised trial is a cohort study with an assigned exposure, and every problem that affects cohort studies applies to it 18.

Person-time. If participants are followed for unequal periods — staggered entry, differential withdrawal, administrative censoring at a common date — counting events without person-time denominators gives a misleading comparison. This situation is routine in trials in which recruitment extends over several years.

Competing risks. A participant who dies of another cause cannot experience the outcome of interest. Where competing events are common, a naive analysis overstates the cumulative incidence of the outcome of interest, and the choice between cause-specific and subdistribution approaches is a design-stage decision rather than an analytic afterthought.

Loss to follow-up. Randomisation balances the arms at baseline and offers no protection thereafter. Differential loss reintroduces precisely the kind of confounding that randomisation was intended to remove, and it is more likely when one arm is more burdensome 16,27.

Duration. Questions about durable effects are answered through long follow-up of a published cohort 15. A general-practice cohort of 46,000 women followed for 25 years was used to estimate mortality associated with oral contraceptive use — a question no trial would have been funded to follow that far, and one that required stable record linkage rather than trial infrastructure 21.

The implication for a trial team planning extended follow-up is that it should be planned as a cohort study, with a cohort study’s attention to ascertainment and attrition, and reported as one. See biostatistics and the analysis plan for how these decisions are pre-specified.

The protection conferred by randomisation

Randomisation confers precisely one protection: it makes the arms comparable in expectation at the moment of assignment, including on confounders that were neither measured nor anticipated 14. That benefit is substantial, but it is also the entire benefit.

It does not make a small trial balanced — expectation is not realisation, and chance imbalance in a 40-participant trial is common. It does not protect against anything that occurs after assignment: differential dropout, unblinded outcome assessment, post-randomisation exclusions, competing risks 16,27. It does not make the trial population representative of the treated population, which is a selection question entirely unaffected by randomisation. Nor does it address measurement error in the outcome, which biases the estimate regardless of how assignment was performed.

The constructive application is to list the threats to the trial’s validity and mark those that randomisation addresses. Usually these are one or two, and the remainder require blinding, complete follow-up, pre-specification and an epidemiologically characterised eligibility frame. A trial team that believes randomisation addresses the entire list is likely to under-invest in the other safeguards.

Threats to validity, and whether randomisation addresses them

ThreatAddressed by randomisation?What addresses it instead
Confounding at baseline, measured and unmeasuredYes, in expectation—
Chance imbalance in a small trialNo — expectation is not realisationStratification, minimisation, covariate adjustment specified in advance
Differential loss to follow-upNoRetention design, complete ascertainment, sensitivity analysis under alternative missingness assumptions
Competing risksNoA pre-specified competing-risks analysis rather than a naive cumulative incidence
Outcome measurement error or biased assessmentNoBlinded outcome assessment, standardised instruments, central adjudication
Trial population differing from the treated populationNoAn epidemiologically characterised eligibility frame and explicit generalisability discussion

Randomisation’s guarantee is comparability of arms in expectation at the moment of assignment. Everything downstream of assignment requires separate design features.

External and historical comparisons

A randomised comparison is sometimes unavailable — in a very rare disease, a single-arm oncology study, or a context in which withholding treatment is not acceptable. The question is then when a non-randomised comparison is defensible, and the answer is: when the natural history is well characterised, stable over the relevant period and ascertained by comparable means, and when the outcome is not substantially dependent on judgement.

Each condition is important. Natural history that has changed because supportive care improved makes a historical control optimistic about the past and pessimistic about the intervention, or the reverse. Outcomes ascertained by different means — imaging intervals, laboratory assays, diagnostic criteria — are not the same outcome. A judgement-dependent outcome assessed by individuals aware of group allocation is the source of most of the bias in this literature 16,27.

The decisive factors in practice are pre-specification and a comparator cohort assembled before the study’s own results are known. A comparison group chosen after the single-arm result has been seen is a selected comparison, and no statistical adjustment corrects selection on the outcome 16. Where the comparison supports a health-economic claim, the requirements are stricter still — see our page on health economics in trials.

Matching the design to the research question

The design should be derived from the question, in the following order.

First, what is the sampling basis? If participants must be identified by their outcome because the outcome is rare, a case-control design is indicated and the estimate will be an odds ratio. If a group can be defined by exposure and followed, a cohort design is indicated and rates can be estimated.

Second, what is expensive? If the exposure measurement is expensive and the outcome is uncommon, a nested case-control or case-cohort design within an existing cohort is usually appropriate, and the number of cases determines precision.

Third, how many outcomes are to be studied? A single outcome favours a nested case-control design; several favour a case-cohort design, because a single random subcohort serves them all.

Fourth, does temporal order need to be established? If so, a cross-sectional design is excluded regardless of its convenience.

Fifth, what will a reader require in order to accept the findings? The answer determines the design features on which economies cannot be made — complete case ascertainment, a control sampling scheme that can be described in one sentence, and outcome ascertainment that does not depend on exposure status. Our cohort studies page and study design support go into each of these.

The design paragraph of an observational sub-study protocol (figures below are illustrative)

Names a data source

We will conduct a retrospective analysis of the trial biobank to investigate the association between the baseline biomarker and the occurrence of the primary safety event. Cases will be identified from the trial safety database and compared with other trial participants. Logistic regression will be used to estimate the association, adjusting for relevant baseline covariates.

No design named. “Retrospective analysis of the biobank” names a data source. It does not say what is being sampled on, which determines what can be estimated.

“Compared with other trial participants” is not a control sampling scheme. Whether controls are survivors, a baseline sample, or risk-set sampled changes what the odds ratio means.

Risk-set timing ignored. Without sampling controls from those at risk when each case occurred, the estimate does not correspond to a rate ratio.

No masking of the assay. A laboratory that is aware of case status can bias a measurement unintentionally.

Unconditional regression on matched data. If matching is used, unadjusted unconditional logistic regression attenuates the exposure effect, and this plan does not say which model is being fitted.

Precision unaddressed. The paragraph implies the large cohort gives power, when precision is governed by the case count.

Names a design

This is a nested case-control study within the randomised cohort. Cases are all participants with an adjudicated primary safety event occurring between randomisation and the common close-out date, identified from the adjudication committee record rather than from site reporting, so that ascertainment does not depend on site reporting behaviour. For each case, three controls are sampled at random from participants still under follow-up and event-free at the time the case event occurred, matched on randomised arm and on recruitment wave; the sampling is with replacement across cases, so a participant may serve as a control for more than one case and may later become a case. Baseline biomarker concentration is assayed in the resulting case and control samples only, in a single batch, with case and control status masked to the laboratory and with samples ordered randomly within the batch. The primary analysis is conditional logistic regression on the matched sets, with the biomarker entered as a continuous variable and with a pre-specified secondary analysis by tertile; the matching variables are not entered as covariates, since conditioning on the matched set already accounts for them. Because controls are sampled from those at risk at the time of each case event, the resulting odds ratio estimates a rate ratio. The number of cases, not the size of the parent cohort, determines precision: with the 90 adjudicated events anticipated, the study has power to detect the pre-specified effect size stated in Section 7.

The design is named, so a reader knows immediately what was sampled on and what the estimate will be.

Control sampling is specified in a single readable sentence, including risk-set timing, which is what licenses the rate ratio interpretation.

Case ascertainment is taken from adjudication rather than site reporting, so it does not vary with site behaviour.

Assay masking and random ordering within one batch remove two of the commonest sources of differential measurement error.

Conditional logistic regression is specified with the matching variables correctly left out as covariates, which is the analysis the design implies.

Precision is attributed to the case count, which sets a realistic expectation and makes the power statement checkable.

A reviewer reading the first paragraph cannot determine what estimate is being produced or whether it is interpretable. The second states a design, a sampling scheme and a matched analysis that follow from one another — and only this version is likely to withstand statistical review.

Selection of the reporting guideline for each design

Using the wrong reporting guideline is a common and avoidable error. CONSORT governs randomised trials, and its items presuppose assignment, allocation concealment and a flow diagram built around randomisation 8. An observational study reported against CONSORT will omit the items that are relevant to it and claim a structure it does not have.

STROBE is the observational equivalent, with separate checklists for cohort, case-control and cross-sectional designs because the items differ 9,10. The items most often omitted in trial-adjacent observational work are the eligibility and selection description, the handling of missing data, the number of participants at each stage, and an explicit discussion of residual confounding and its likely direction.

For a trial with an extended observational follow-up phase, both guidelines should be applied: CONSORT 2025 for the randomised phase and STROBE for the follow-up, with an explicit statement of the point at which the protection of randomisation ended. Readers require that statement, yet it is rarely provided.

Key points

Key points

Epidemiological designs are not fallbacks for situations in which randomisation fails; they answer questions that a randomised comparison cannot address. The design is determined by the sampling basis: sampling on exposure yields a cohort and rates, whereas sampling on outcome yields a case-control study and an odds ratio whose meaning depends on control sampling. Where an exposure is expensive to measure and the outcome uncommon, the nested case-control design is the efficient option — one published example measured exposure in 74 cases and 147 controls from a parent cohort of 25,802, under 1% of the cohort — and precision is determined by the number of cases rather than the size of the cohort. Within a trial, cohort principles continue to apply: person-time, competing risks and differential loss to follow-up all affect the analysis, and randomisation protects only against baseline confounding, in expectation, at the moment of assignment. Questions about durable effects require long follow-up, as in the general-practice cohort of 46,000 women followed for 25 years to estimate mortality associated with oral contraceptive use. Each phase should be reported against the appropriate guideline, with a statement of where the protection conferred by randomisation ended.

Application to your study

Application to your study

  1. The research question should be specified before the design. The sampling basis should then be identified; that single decision eliminates most candidate designs and determines the measure of effect.
  2. Where the exposure is expensive to measure, a nested case-control or case-cohort design should be considered. A nested case-control design suits a single outcome; a case-cohort design is preferable when a single random subcohort must serve several outcome questions.
  3. Control sampling should be specified in a single sentence. The sentence should state the source population, the timing and the matching variables. If such a sentence cannot be written, the odds ratio has no clear interpretation.
  4. Power calculations should be based on the number of cases, not on cohort size. The parent cohort indicates what is available; the number of cases determines what can be concluded.
  5. The validity threats addressed by randomisation should be identified. The threats should be listed, the one or two addressed by randomisation marked, and the remainder managed through blinding, retention design and pre-specification.
  6. Extended follow-up should be planned as a cohort study from the outset. The plan should specify the ascertainment method, person-time, competing risks and the point at which randomisation ceases to protect the comparison.
  7. The reporting guideline should be selected according to the design rather than the parent study. STROBE’s cohort, case-control or cross-sectional checklist applies to observational phases, and CONSORT to the randomised phase.

Frequently asked questions

The distinction lies in the sampling basis. A cohort study starts from exposure status and follows participants forward to observe who develops the outcome, which permits estimation of incidence and therefore of risk and rate ratios. A case-control study starts from outcome status — people who have the disease and people who do not — and ascertains exposure retrospectively, which yields an odds ratio. The practical consequence is that cohort designs suit common outcomes and rare exposures, whereas case-control designs suit rare outcomes and common exposures. Cohort studies can be prospective, retrospective or ambidirectional, but that refers to when the data were collected relative to the study’s start, not to the direction of the inference, which always runs from exposure to outcome.

A case-control study conducted inside a defined cohort, with controls sampled from that same cohort. It is appropriate when the outcome is uncommon and the exposure is expensive to measure — a stored biomarker, a tissue assay, an exposure requiring record abstraction. Its principal advantage is efficiency: in one published example, exposure was measured in 74 cases and 147 controls drawn from a parent cohort of 25,802 recruited from 1974, which is under 1% of the cohort. The design yields an answer that measuring the entire cohort would not have been funded to produce. The cost is precision, which is governed by the number of cases rather than the cohort size, and the design requires complete case ascertainment and a defensible control sampling scheme.

No. Randomisation makes the arms comparable in expectation at the moment of assignment, including on unmeasured confounders. That is its entire guarantee. It does not guarantee balance in a small trial, where chance imbalance is common; it does not address differential loss to follow-up, competing risks or post-randomisation exclusions; it does not reduce outcome measurement error; and it provides no assurance that the trial population resembles the population that will receive the treatment. Each of those requires its own design feature — stratification, retention planning, blinded assessment, a characterised eligibility frame. A team that regards randomisation as addressing the entire list is likely to under-invest in the remainder.

Two to four for most purposes, and the marginal return beyond about four is small. The reason lies in the behaviour of precision: with a fixed number of cases, adding controls improves the standard error rapidly at first and then plateaus, so moving from one control per case to two or three yields a substantial gain, whereas moving from four to eight yields little. The published nested case-control example used 147 controls for 74 cases, a ratio of roughly two to one, which is a typical and reasonable choice. The more consequential decision concerns not how many controls are selected but how they are sampled — from whom, at what point in time, and matched on what — because that determines whether the odds ratio has a rate ratio interpretation.

When the natural history is well characterised and stable over the relevant period, outcome ascertainment in the comparison group is genuinely comparable to that in the study, the outcome does not depend heavily on assessor judgement, and the comparison cohort was assembled and pre-specified before the study’s own results were known. Each condition is important: supportive care that improved between the historical period and the present biases the comparison; outcomes measured with different imaging intervals or diagnostic criteria are different outcomes; and a judgement-dependent outcome assessed without blinding is the source of most of the bias in this literature. A comparison group chosen after the single-arm result has been seen constitutes selection on the outcome, which no statistical adjustment corrects.

Long enough for the outcome to accumulate in sufficient numbers, which depends entirely on the incidence rate and the effect size to be detected — not on any conventional duration. Person-time provides a useful framework: a cohort of 10,000 followed for five years and one of 2,000 followed for twenty-five years yield similar person-time, but they answer different questions, because the second can detect outcomes with long induction periods and the first cannot. For durable exposure-mortality questions, follow-up is measured in decades: a general-practice cohort of 46,000 women was followed for 25 years to estimate mortality associated with oral contraceptive use, which no trial would have been funded to do.

STROBE, with the checklist matching the design — cohort, case-control or cross-sectional, since the items differ between them. CONSORT is not appropriate: its items presuppose random assignment, allocation concealment and a flow diagram organised around randomisation, so an observational study reported against it omits the relevant items and claims a structure it does not have. For a trial with an extended observational follow-up phase, both should be used, CONSORT for the randomised phase and STROBE for the follow-up, with an explicit statement of the point at which the protection of randomisation ended. The STROBE items most often omitted in trial-adjacent work are the selection description, missing data handling, participant numbers at each stage, and the direction of likely residual confounding.

The term derives from the Roman military unit: a cohort was a body of around 300 to 600 men, and ten cohorts made a legion. The borrowed sense is apt and instructive, because it captures the defining feature of the design — a defined group of people who are identified together and then followed forward through time together. That feature makes the person-time denominator meaningful and makes attrition a threat rather than an inconvenience: once some members have been lost differentially, the cohort no longer corresponds to the group defined at the start.

References

  1. Schauberger G, Klug SJ, Berger M. Random forests for the analysis of matched case-control studies. BMC Bioinformatics. 2024;25(1):253. doi:10.1186/s12859-024-05877-5 read 9 October 2026. doi.org/10.1186/s12859-024-05877-5
  2. Zeng L, Brignardello-Petersen R, Hultcrantz M, Mustafa RA, Murad MH, Iorio A, et al. GRADE Guidance 34: update on rating imprecision using a minimally contextualized approach. Journal of Clinical Epidemiology. 2022;150:216-224. doi:10.1016/j.jclinepi.2022.07.014 read 9 October 2026. doi.org/10.1016/j.jclinepi.2022.07.014
  3. Schunemann HJ, Neumann I, Hultcrantz M, Brignardello-Petersen R, Zeng L, Murad MH, et al. GRADE guidance 35: update on rating imprecision for assessing contextualized certainty of evidence and making decisions. Journal of Clinical Epidemiology. 2022;150:225-242. doi:10.1016/j.jclinepi.2022.07.015 read 9 October 2026. doi.org/10.1016/j.jclinepi.2022.07.015
  4. Wan F, Colditz GA, Sutcliffe S. Matched Versus Unmatched Analysis of Matched Case-Control Studies. American Journal of Epidemiology. 2021;190(9):1859-1866. doi:10.1093/aje/kwab056 read 9 October 2026. doi.org/10.1093/aje/kwab056
  5. Guyatt GH, Oxman AD, Kunz R, Brozek J, Alonso-Coello P, Rind D, et al. GRADE guidelines 6. Rating the quality of evidence - imprecision. Journal of Clinical Epidemiology. 2011;64(12):1283-1293. doi:10.1016/j.jclinepi.2011.01.012 read 9 October 2026. doi.org/10.1016/j.jclinepi.2011.01.012
  6. Guyatt G, Oxman AD, Akl EA, Kunz R, Vist G, Brozek J, et al. GRADE guidelines: 1. Introduction - GRADE evidence profiles and summary of findings tables. Journal of Clinical Epidemiology. 2011;64(4):383-394. doi:10.1016/j.jclinepi.2010.04.026 read 9 October 2026. doi.org/10.1016/j.jclinepi.2010.04.026
  7. Balshem H, Helfand M, Schunemann HJ, Oxman AD, Kunz R, Brozek J, et al. GRADE guidelines: 3. Rating the quality of evidence. Journal of Clinical Epidemiology. 2011;64(4):401-406. doi:10.1016/j.jclinepi.2010.07.015 read 9 October 2026. doi.org/10.1016/j.jclinepi.2010.07.015
  8. Schulz KF, Altman DG, Moher D. CONSORT 2010 Statement: updated guidelines for reporting parallel group randomised trials. Trials. 2010;11(1):32. doi:10.1186/1745-6215-11-32 read 9 October 2026. doi.org/10.1186/1745-6215-11-32
  9. von Elm E, Altman DG, Egger M, Pocock SJ, Gotzsche PC, Vandenbroucke JP; STROBE Initiative. Strengthening the reporting of observational studies in epidemiology (STROBE) statement: guidelines for reporting observational studies. BMJ. 2007;335(7624):806-808. doi:10.1136/bmj.39335.541782.AD read 9 October 2026. doi.org/10.1136/bmj.39335.541782.AD
  10. von Elm E, Altman DG, Egger M, Pocock SJ, Gotzsche PC, Vandenbroucke JP; STROBE Initiative. The Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) statement: guidelines for reporting observational studies. Epidemiology. 2007;18(6):800-804. doi:10.1097/EDE.0b013e3181577654 read 9 October 2026. doi.org/10.1097/EDE.0b013e3181577654
  11. Ridker PM, Cook NR, Lee I-M, Gordon D, Walter JM, Buring JE, et al. A randomized trial of low-dose aspirin in the primary prevention of cardiovascular disease in women. New England Journal of Medicine. 2005;352(13):1293-1304. doi:10.1056/NEJMoa050613 read 9 October 2026. doi.org/10.1056/NEJMoa050613
  12. Grimes DA, Schulz KF. Compared to what? Finding controls for case-control studies. The Lancet. 2005;365(9468):1429-1433. doi:10.1016/S0140-6736(05)66379-9 read 9 October 2026. doi.org/10.1016/S0140-6736(05)66379-9
  13. Ioannidis JP. Contradicted and initially stronger effects in highly cited clinical research. JAMA. 2005;294(2):218-228. doi:10.1001/jama.294.2.218 read 9 October 2026. doi.org/10.1001/jama.294.2.218
  14. Lawlor DA, Davey Smith G, Ebrahim S. Commentary: the hormone replacement-coronary heart disease conundrum: is this the death of observational epidemiology? International Journal of Epidemiology. 2004;33(3):464-467. doi:10.1093/ije/dyh124 read 9 October 2026. doi.org/10.1093/ije/dyh124
  15. Doll R, Peto R, Boreham J, Sutherland I. Mortality in relation to smoking: 50 years' observations on male British doctors. BMJ. 2004;328(7455):1519. doi:10.1136/bmj.38142.554479.AE read 9 October 2026. doi.org/10.1136/bmj.38142.554479.AE
  16. Grimes DA, Schulz KF. Bias and causal associations in observational research. The Lancet. 2002;359:248-252. read 9 October 2026. qmplus.qmul.ac.uk
  17. Schulz KF, Grimes DA. Case-control studies: research in reverse. The Lancet. 2002;359(9304):431-434. doi:10.1016/S0140-6736(02)07605-5 read 9 October 2026. doi.org/10.1016/S0140-6736(02)07605-5
  18. Grimes DA, Schulz KF. Cohort studies: marching towards outcomes. The Lancet. 2002;359:341-345. doi:10.1016/S0140-6736(02)07500-1 read 9 October 2026. doi.org/10.1016/S0140-6736(02)07500-1
  19. King G, Zeng L. Estimating risk and rate levels, ratios and differences in case-control studies. Statistics in Medicine. 2002;21(10):1409-1427. doi:10.1002/sim.1032 read 9 October 2026. doi.org/10.1002/sim.1032
  20. Zondervan KT, Cardon LR, Kennedy SH. What makes a good case-control study? Design issues for complex traits such as endometriosis. Human Reproduction. 2002;17:1415-1423. read 9 October 2026. ebm-netzwerk.de
  21. Beral V, Hermon C, Kay C, Hannaford P, Darby S, Reeves G. Mortality associated with oral contraceptive use: 25 year follow up of cohort of 46 000 women from Royal College of General Practitioners' oral contraception study. BMJ. 1999;318:96-100. read 9 October 2026. qmplus.qmul.ac.uk
  22. Rothman N, Cantor KP, Blair A, Bush D, Brock JW, Helzlsouer K, et al. A nested case-control study of non-Hodgkin lymphoma and serum organochlorine residues. The Lancet. 1997;350:240-244. read 9 October 2026. qmplus.qmul.ac.uk
  23. Bland JM, Altman DG. Regression towards the mean. BMJ. 1994;308:1499. read 9 October 2026. qmplus.qmul.ac.uk
  24. Wacholder S, McLaughlin JK, Silverman DT, Mandel JS. Selection of controls in case-control studies, I: principles. American Journal of Epidemiology. 1992;135(9):1019-1028. read 9 October 2026. med.libretexts.org
  25. Wacholder S, Silverman DT, McLaughlin JK, Mandel JS. Selection of controls in case-control studies, II: types of controls. American Journal of Epidemiology. 1992;135(9):1029-1041. read 9 October 2026. med.libretexts.org
  26. Rodrigues L, Kirkwood BR. Case-control designs in the study of common diseases: updates on the demise of the rare disease assumption and the choice of sampling scheme for controls. International Journal of Epidemiology. 1990;19(1):205-213. doi:10.1093/ije/19.1.205 read 9 October 2026. doi.org/10.1093/ije/19.1.205
  27. Sackett DL. Bias in analytic research. Journal of Chronic Diseases. 1979;32:51-63. read 9 October 2026. qmplus.qmul.ac.uk
  28. Prentice RL, Pyke R. Logistic disease incidence models and case-control studies. Biometrika. 1979;66:403-411. read 9 October 2026. kiwix.lema.org
  29. Miettinen O. Estimability and estimation in case-referent studies. American Journal of Epidemiology. 1976;103(2):226-235. doi:10.1093/oxfordjournals.aje.a112220 read 9 October 2026. doi.org/10.1093/oxfordjournals.aje.a112220
  30. Doll R, Hill AB. Smoking and carcinoma of the lung; preliminary report. British Medical Journal. 1950;2(4682):739-748. doi:10.1136/bmj.2.4682.739 read 9 October 2026. doi.org/10.1136/bmj.2.4682.739

Every source above is a peer-reviewed article, a publisher’s record of one, or a standard issued by the body that owns it. Each carries the date it was last read. Where a standard moves, this article is revised rather than left up with a note.

How to cite this article

Pick your referencing style and copy it. Your university or target journal may vary the punctuation — check its guide if it has one.

Pubrica Academy. (2026, October 9). Epidemiological Designs for Clinical Trials: Cohort, Case-Control and Nested Designs in Trial Programmes. Pubrica. https://pubrica.com/academy/research/epidemiology-designs-for-clinical-trials/

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.

Design selection worksheet

Four questions, to be answered in order before a data source is chosen, because the answers determine what estimate the study can produce and therefore the purposes for which it can be used.

EPIDEMIOLOGICAL DESIGN SELECTION WORKSHEET

Q0. THE QUESTION, IN ONE SENTENCE
   ____________________________________________________________
   Exposure / intervention: ____________________________________
   Outcome, with definition and ascertainment method: ___________
   Population: _________________________________________________
   Time frame: _________________________________________________

Q1. WHAT ARE YOU SAMPLING ON?
   [ ] Exposure, then follow forward      -> COHORT
   [ ] Outcome, then look back            -> CASE-CONTROL
   [ ] Outcome inside a defined cohort    -> NESTED CASE-CONTROL
   [ ] Cases + random subcohort           -> CASE-COHORT
   [ ] Both at once                       -> CROSS-SECTIONAL
   [ ] Time                               -> BEFORE-AFTER / ITS
   Measure this design yields: _________________________________

Q2. WHAT IS EXPENSIVE?
   Cost of measuring exposure per person: ______________
   Cost of follow-up per person-year: ______________
   Outcome frequency: ______ per ______ person-years
   If exposure is expensive AND outcome uncommon, prefer a
   nested case-control or case-cohort design inside an existing
   cohort.  Decision: __________________________________________

Q3. HOW MANY OUTCOMES?
   Number of distinct outcome questions: ______
   One   -> nested case-control is efficient
   Several -> case-cohort (one subcohort serves all)
   Decision: ___________________________________________________

Q4. DOES TEMPORAL ORDER HAVE TO BE ESTABLISHED?
   [ ] Yes - cross-sectional is excluded
   [ ] No

IF CASE-CONTROL OR NESTED CASE-CONTROL, COMPLETE THIS:
   Case definition: ____________________________________________
   Case ascertainment source: __________________________________
   [ ] Ascertainment does not depend on exposure status
   Controls sampled FROM: ______________________________________
   Controls sampled AT: [ ] baseline [ ] risk-set at case time
                        [ ] end of follow-up
   Matched on: _________________________________________________
   Controls per case: ______  (2-4 is usually sufficient)
   Can a control later become a case?  [ ] yes  [ ] no
   Analysis model: [ ] conditional logistic regression
                   [ ] unconditional, adjusted - justify: ______
   Measure the odds ratio will estimate: _______________________

IF COHORT (including extended trial follow-up), COMPLETE THIS:
   Entry criterion and date: ___________________________________
   Exit criteria: [ ] outcome [ ] death [ ] withdrawal
                  [ ] administrative censoring on __________
   Person-time used as denominator?  [ ] yes
   Competing events expected: __________________________________
   Competing-risks approach pre-specified: _____________________
   Expected loss to follow-up: ______%  differential by exposure?
     [ ] no  [ ] yes - sensitivity analysis: ___________________
   For trial follow-up: date at which randomisation stops
   protecting the comparison: ______________

PRECISION
   Expected number of CASES / EVENTS: ______
   (This, not the cohort size, sets your precision.)
   Detectable effect size with that number: ______

REPORTING
   Guideline: [ ] STROBE cohort  [ ] STROBE case-control
              [ ] STROBE cross-sectional  [ ] CONSORT (randomised)
   If the study has both phases, both are required.

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 matches the design to the question before any data source is considered, which is the stage at which most observational sub-studies fail — by naming a database rather than a sampling scheme. For trial biobanks, nested case-control and case-cohort designs are specified with the control sampling, matching and conditional analysis stated, so that the resulting estimate has a defined interpretation, and the study is powered on expected cases rather than on cohort size. Each phase is reported against the appropriate guideline, with a statement of where the protection conferred by randomisation ended.

Find something else

Search the Pubrica Academy

Access is free and requires no account. Enter a topic, or open the full library to filter by category, sub-topic or resource type.

Pubrica can review the questions that surround a trial and advise which epidemiological design is capable of answering each of them.

A scoping assessment is free and takes two business days. It provides a written assessment of what the work requires and which specialist would undertake it.

Get a free quote

Regulations

Check your project against this rule

  1. 1Your work
  2. 2Your details
  3. 3Send
What do you need?

Material you send is held under signed confidentiality, with access limited to the assigned team and encrypted transfer. It is not used to train anything and is not passed to third-party tools. Ask for the agreement before you send anything you would rather cover first.