Study Designs and Their Statistical Implications

Overview

A study design is the structure used to connect a research question with observations. It determines who enters the study, when exposure and outcome are measured, whether the investigator assigns an intervention and which comparisons can be estimated directly.

Clinical research is commonly divided into experimental studies, in which investigators assign an intervention or exposure, and observational studies, in which investigators observe exposures that occur without assignment by the research team [1]. Within these broad groups, randomised trials, cohort studies, case-control studies and cross-sectional studies have different statistical implications.

The same two-by-two table can appear in more than one design, but its interpretation may differ. A risk ratio estimated in a well-conducted randomised trial has a different causal basis from the same numerical risk ratio estimated in an observational cohort. Study design therefore comes before statistical testing.

Why this matters

A statistical method cannot repair a design that does not answer the intended question.

Examples include:

• estimating prevalence from a case-control sample, even though participants were selected according to outcome status;
• analysing patients in a cluster-randomised trial as independent observations;
• interpreting a cross-sectional association as evidence that the exposure preceded the outcome;
• reporting an odds ratio from a case-control study as though it were an observed risk ratio; and
• attributing an observational group difference to treatment without considering confounding.

The design determines which denominators are available, whether incidence can be measured, how observations are related and what assumptions are needed for interpretation.

Begin with three design questions

Before naming a design, ask:

1. Did the investigator assign the intervention or exposure?
2. Were participants selected according to exposure, outcome or neither?
3. Were exposure and outcome measured over time or at one assessment period?

These questions are more informative than labels such as “prospective” or “retrospective” alone.

“Prospective” describes when data are collected relative to the study’s start. It does not by itself identify whether a study is a trial, cohort or another design. A retrospective cohort still begins conceptually with exposure groups and follows their recorded experience towards outcomes.

Experimental studies

In an experimental study, the investigator assigns an intervention.

Individually randomised controlled trial

In an individually randomised controlled trial, eligible participants are assigned to comparison groups using a random mechanism. Proper random sequence generation prevents predictable allocation and helps balance both measured and unmeasured prognostic factors between groups on average [2].

For the medication-review question, 1,000 participants could be individually randomised to:

• pharmacist-led medication review; or
• usual discharge care.

Participants would then be followed for 30 days.

Statistical implications include:

• the participant is the unit of randomisation and usually the unit of analysis;
• risks, risk differences and risk ratios can be estimated because denominators are known;
• the primary analysis should generally compare participants according to their allocated groups;
• confidence intervals should reflect the randomised comparison;
• missing outcomes and departures from the allocated intervention must be addressed; and
• adjusted analyses should use prespecified baseline variables rather than data-driven selection alone.

Randomisation does not guarantee perfect numerical balance in one finite trial. It creates a known assignment process that supports valid inference when preserved.

Cluster-randomised trial

Sometimes the intervention is delivered to an entire ward, clinic or hospital. The cluster, rather than the patient, is randomised.

If wards are randomised to implement pharmacist review, patients within the same ward may receive similar care and have correlated outcomes. The analysis must account for clustering using an appropriate cluster-level or individual-level method.

Ignoring clustering usually underestimates uncertainty because the nominal number of patients overstates the amount of independent information.

Non-randomised intervention study

A hospital may introduce the service in one ward and compare outcomes with another ward or with an earlier period.

The investigator still assigns or implements an intervention, but without random allocation. Differences between wards, periods or patient groups may confound the comparison. Interrupted time-series or controlled before-and-after designs may be stronger than a single uncontrolled before-and-after comparison, but their analyses must reflect time trends and repeated observations.

Observational studies

In an observational study, the investigator does not assign the exposure. Observational designs are valuable when randomisation is unethical, infeasible or unnecessary, but causal interpretation usually requires stronger assumptions about confounding and selection.

Cohort study

A cohort study identifies participants according to exposure status or exposure history and follows them conceptually from exposure towards outcome [3].

For the scenario, a cohort study could compare:

• patients who received pharmacist-led review during routine care; and
• eligible patients who received usual care.

The cohort may be:

• prospective, with exposure recorded at discharge and outcomes collected subsequently; or
• retrospective, with both exposure and follow-up reconstructed from existing records.

Both are cohort studies because the direction of inquiry runs from exposure to outcome.

Cohort studies can directly estimate:

• cumulative incidence, also called risk, over a defined period;
• incidence rates when person-time is available;
• risk differences;
• risk ratios;
• rate differences or rate ratios; and
• time-to-event measures when follow-up times vary.

Important statistical issues include confounding, loss to follow-up, changes in exposure, competing events and unequal follow-up.

In this scenario, patients who receive pharmacist review may be older, take more medicines or have more complex disease. Statistical adjustment can address measured baseline differences under assumptions, but it cannot guarantee removal of unmeasured or poorly measured confounding.

Case-control study

A case-control study begins by selecting people according to outcome status and then compares their previous exposure histories [4].

The hospital could select:

• cases: eligible patients with a medication-related readmission within 30 days; and
• controls: eligible patients from the same source population who could have become cases but did not meet the case definition at the relevant selection time.

The ordinary case-control sample does not contain the source-population denominators required to calculate risks directly. The usual effect measure is an odds ratio, comparing the odds of previous pharmacist review among cases with the corresponding odds among controls.

Control selection is central. Controls should represent the exposure distribution in the population that produced the cases. Selecting convenient controls from a different referral pathway can distort the odds ratio.

If cases and controls are individually matched, the analysis must preserve the matched structure. Treating matched observations as independent can produce an inappropriate estimate or standard error.

Cross-sectional study

A cross-sectional study measures exposure and outcome during a defined assessment period without following individuals from exposure to a new outcome [5].

The hospital could survey recently discharged patients at one service-review point to estimate:

• the prevalence of unresolved medication discrepancies;
• the proportion who report receiving pharmacist review; and
• the association between current discrepancy status and reported service receipt.

Cross-sectional data are well suited to prevalence estimation. They often provide limited evidence about temporal order because exposure and outcome are assessed at the same time or over an overlapping period.

Suitable effect measures may include:

• prevalence difference;
• prevalence ratio; or
• prevalence odds ratio.

A prevalence odds ratio should not be labelled a risk ratio. Cross-sectional prevalence also reflects both the occurrence and duration of a condition, so it is not equivalent to incidence.

Ecological study

An ecological study analyses groups rather than individuals. The hospital might compare ward-level pharmacist staffing with ward-level readmission rates.

The unit of analysis is the ward. An association between ward-level variables does not establish that individual patients who received pharmacist review had lower risk. Drawing an individual-level conclusion from a group-level association is the ecological fallacy.

With only a small number of wards, statistical power and adjustment options may also be limited.

Designs for other clinical questions

The major designs above do not cover every medical question.

A diagnostic-accuracy study compares an index test with a reference standard in the same participants. The paired structure must be retained when estimating sensitivity, specificity or comparing tests.

A prognosis study commonly uses a cohort assembled at a defined clinical starting point and follows participants for future outcomes. Time origin, censoring and competing events matter.

A case report or case series describes unusual or informative clinical observations. Without a suitable comparison group, it cannot estimate a comparative treatment effect.

Qualitative studies address experiences, meanings and processes using different sampling and analytical traditions. They should not be forced into a quantitative hierarchy designed for effect estimation.

Statistical implications by design

Table 1. Common designs and their direct statistical implications

Note: The table gives common starting points. Special sampling designs and analytical methods can support additional estimands when the necessary information and assumptions are available.

The unit of analysis must match the design

The unit of analysis is the entity represented by each independent contribution to the main analysis.

Examples include:

• participant in an individually randomised trial;
• ward in a simple cluster-level analysis;
• matched set in a matched case-control study;
• person-visit in a longitudinal dataset, with correlation within person modelled; and
• hospital in an ecological study.

Counting every measurement as independent when several measurements come from one person or cluster usually produces standard errors that are too small.

Time determines the denominator

A 30-day risk requires:

• a defined time origin;
• participants at risk at that origin;
• a defined event;
• a 30-day follow-up window; and
• known outcome status or an explicit missing-data strategy.

When follow-up time differs substantially, person-time rates or survival methods may be more appropriate than treating everyone as though they had equal follow-up.

Design determines the role of confounding

Random allocation aims to break the systematic relationship between treatment assignment and baseline prognosis.

In observational studies, exposure groups may differ before follow-up begins. A confounder is a pre-exposure common cause, or a factor representing such a cause, of both the exposure and outcome. Failure to address relevant confounding can distort the exposure–outcome comparison.

Adjustment should be guided by the research question and subject-matter knowledge. Selecting variables solely because their univariable p-values are below a threshold is not a sound confounder-selection strategy.

Data structure

Simulated randomised medication-review trial

simulated data

Table 2. Example participant-level records

participant_id	allocated_group	review_completed	readmission_30d
MR001	Pharmacist review	Yes	No
MR002	Usual care	Not applicable	Yes
MR003	Pharmacist review	No	No
MR004	Usual care	Not applicable	No

Note: Each row represents one individually randomised participant. The primary group variable is allocation, not whether the review was completed.

Table 3. How the dataset would differ by design

Design	Essential row-level information
Randomised trial	Allocation, intervention received, outcome, follow-up status and prespecified baseline variables
Cohort	Exposure status or history, outcome, time origin, follow-up and baseline confounders
Case-control	Case or control status, previous exposure and matching variables where applicable
Cross-sectional	Sampling information, current or period-specific exposure and outcome measurements

Note: The dataset structure follows the design. It should not be reconstructed after analysis from an ambiguous spreadsheet.

Worked example

Why matching, clustering and repeated measurements change the analysis MMed extension

Design features create dependence that must be represented statistically.

• Matching: A matched case-control study deliberately links each case to one or more controls. Conditional logistic regression or another matched analysis may be required.
• Clustering: Patients within the same ward or clinic may share staff, protocols and patient mix. Cluster-robust standard errors, mixed models, generalised estimating equations or cluster-level methods may be appropriate.
• Repeated measurements: Several observations from one participant are correlated. Repeated-measures models must distinguish within-person change from between-person differences.
• Sampling weights: Unequal selection probabilities require design-aware estimation when the objective is population inference.

These features should be specified during study planning because they affect sample-size requirements, data structure, estimands and standard errors.

Suggested reporting

CONSORT 2025 provides current reporting guidance for randomised trials [7]. The Strengthening the Reporting of Observational Studies in Epidemiology statement covers cohort, case-control and cross-sectional studies [8]. Reporting guidelines improve transparency but do not convert a weak design into a strong one.

For an observational cohort, the Methods section would also need to define exposure assignment in routine care, baseline confounders, follow-up, missing data and the adjustment model. The Results section should distinguish crude from adjusted estimates and avoid causal wording unless the design and assumptions justify it.

Common mistakes

Knowledge check

Patients are grouped according to whether they received pharmacist review and then followed for 30-day readmission. Investigators did not assign the service. What is the design?

Answer and reasoning

It is a cohort study. Participants are classified by exposure and followed conceptually from exposure towards outcome. It is observational because the investigators did not allocate the review.

Investigators select 100 readmitted patients and 200 controls, then examine previous pharmacist-review exposure. What effect measure is usually estimated?

Answer and reasoning

The usual measure is an odds ratio. Participants were selected according to outcome status, so the sampled case and control counts do not directly provide the source-population risks required for a risk ratio.

Why can the same risk difference have a different interpretation in a randomised trial and a cohort study?

Answer and reasoning

The arithmetic depends on the group risks, but interpretation also depends on how groups were formed. Random allocation supports comparability through a known chance mechanism. In a cohort, treatment groups may differ in baseline prognosis, so confounding must be considered.

A trial randomises ten hospital wards and enrols 40 patients per ward. Why should the 400 patients not automatically be analysed as independent?

Answer and reasoning

Patients within a ward may receive similar care and have correlated outcomes. The ward is the unit of randomisation, and the analysis must account for within-ward clustering. Ignoring it can make the confidence interval too narrow.

A cross-sectional survey finds that medication discrepancies are more common among patients reporting no pharmacist review. Can it prove that lack of review caused the discrepancies?

Answer and reasoning

No. The study can estimate prevalence and a cross-sectional association, but temporal order may be unclear and confounding may remain. Causal interpretation requires stronger design and assumptions.

Key take-home messages

References

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2. Schulz KF, Grimes DA. Generation of allocation sequences in randomised trials: chance, not choice. Lancet. 2002;359(9305):515–519. https://doi.org/10.1016/S0140-6736(02)07683-3
3. Grimes DA, Schulz KF. Cohort studies: marching towards outcomes. Lancet. 2002;359(9303):341–345. https://doi.org/10.1016/S0140-6736(02)07500-1
4. Schulz KF, Grimes DA. Case-control studies: research in reverse. Lancet. 2002;359(9304):431–434. https://doi.org/10.1016/S0140-6736(02)07605-5
5. Wang X, Cheng Z. Cross-sectional studies: strengths, weaknesses, and recommendations. Chest. 2020;158(1 Suppl):S65–S71. https://doi.org/10.1016/j.chest.2020.03.012
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7. Hopewell S, Chan AW, Collins GS, Hróbjartsson A, Moher D, Schulz KF, et al. CONSORT 2025 statement: updated guideline for reporting randomised trials. BMJ. 2025;389:e081123. https://doi.org/10.1136/bmj-2024-081123
8. von Elm E, Altman DG, Egger M, Pocock SJ, Gøtzsche PC, Vandenbroucke JP, et al. The Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) statement: guidelines for reporting observational studies. PLoS Med. 2007;4(10):e296. https://doi.org/10.1371/journal.pmed.0040296