Randomised Controlled Trial

How randomisation supports a fair comparison

A randomised controlled trial compares interventions by assigning eligible participants to study groups using a chance-based process. This page explains how randomisation protects causal comparisons, how allocation, blinding, follow-up and analysis work together, and how trial evidence can inform clinical and economic decisions.

Randomisation does not make every trial unbiased or automatically relevant to practice. Its value depends on whether the sequence is genuinely random, allocation is concealed, outcomes are measured consistently, participants are retained and the analysis preserves a fair comparison.

Defining the trial question

A trial should begin with a precise question that identifies the population, interventions, comparator, outcomes, follow-up and intended interpretation. These elements determine who is recruited, what is measured and which effect the trial is designed to estimate.

The trial question commonly specifies:

• Population: The patients or participants to whom the result is intended to apply.
• Experimental intervention: The treatment, service, programme or policy being evaluated.
• Comparator: The relevant alternative, such as usual care, placebo or another active intervention.
• Outcomes: The benefits, harms and patient-relevant consequences used to compare groups.
• Time horizon: The period over which outcomes are measured.
• Setting: The clinical, organisational and geographical context of the trial.
• Estimand: The treatment effect the analysis is intended to estimate under specified conditions.

The comparator should represent a meaningful decision option. A trial can estimate an internally valid effect while answering a question that is not useful to patients or decision makers if the comparator is obsolete or irrelevant.

Generating the random allocation sequence

Random sequence generation uses a chance-based method so that each participant's assignment is unpredictable before allocation. Proper randomisation helps distribute measured and unmeasured baseline characteristics between groups without relying on investigator judgement.

Methods may include:

• Simple randomisation.
• Block randomisation to maintain balance over recruitment.
• Stratified randomisation to balance selected prognostic characteristics.
• Minimisation with an appropriate random component.
• Cluster randomisation when groups rather than individuals receive the intervention.

Alternation, date of birth, medical-record number and clinician choice are not genuinely random because assignment may be predicted or influenced. Restricted methods should be designed carefully because small fixed blocks can also make future assignments easier to guess.

Concealing allocation

Allocation concealment prevents recruiters and participants from knowing the next assignment before a participant enters the trial. It protects the enrolment process from conscious or unconscious selection.

Central randomisation and securely controlled automated systems can provide effective concealment. Sequentially numbered, opaque, sealed envelopes may be used when designed and administered rigorously, but they are vulnerable to tampering or procedural failure.

Allocation concealment occurs before assignment and is distinct from blinding after assignment. A trial may be open label while still having adequate allocation concealment.

Blinding after assignment

Blinding reduces the possibility that knowledge of treatment assignment changes care, participant behaviour, outcome assessment or analysis. The people who can be blinded depend on the intervention and setting.

Potentially blinded groups include:

• Participants.
• Clinicians and intervention providers.
• Outcome assessors.
• Data managers.
• Statisticians or adjudication committees.

Blinding may be impossible for surgery, behavioural programmes or service changes. In those cases, the trial should use other protections, such as objective outcomes, blinded outcome assessment, standardised care procedures and prespecified analysis.

The terms single blind and double blind can be ambiguous. Reports should identify exactly who was blinded and how blinding was maintained and assessed.

Delivering the intervention and comparator

The trial should define each intervention in enough detail to support consistent delivery and interpretation. Differences between groups should reflect the intended contrast rather than undocumented differences in follow-up, co-interventions or provider attention.

Relevant information includes:

• Intervention components and dose or intensity.
• Who delivers the intervention and what training is required.
• Timing, frequency and duration.
• Permitted and prohibited co-interventions.
• Adherence and fidelity measures.
• Criteria for treatment modification or discontinuation.
• The content of usual care or the active comparator.

Usual care may vary across sites and over time. Its content should be measured rather than treated as a self-explanatory label.

Selecting outcomes

Trial outcomes should reflect benefits and harms that matter to patients and the decision. Surrogate or intermediate outcomes may be useful when final outcomes take a long time to occur, but their relationship to patient-relevant benefit should be justified.

The protocol should specify:

• The primary outcome.
• Important secondary outcomes.
• Outcome definitions and measurement instruments.
• Assessment time points.
• Who measures each outcome.
• Rules for repeated or multiple events.
• Methods for adjudication.
• The planned analysis metric.

Changing the primary outcome or analysis after seeing results increases the risk of selective reporting. Protocols and statistical analysis plans help distinguish prespecified analyses from exploratory findings.

Determining the sample size

Sample-size planning estimates how many participants are required to address the primary question with acceptable statistical precision or power. It should reflect the outcome, expected event rate or variability, target effect, significance level, power, allocation ratio and anticipated loss to follow-up.

The target difference should be clinically or practically meaningful, not merely the smallest difference that can be detected with available resources. Overly optimistic assumptions about treatment effect or recruitment can produce a trial that cannot answer its question.

For cluster trials, sample size must account for similarity between participants in the same cluster. For trials with repeated measurements or multiple primary outcomes, the calculation should reflect the planned design and analysis.

Following participants after randomisation

Randomisation creates comparable groups at assignment, but differential follow-up can undermine that comparison. Every reasonable effort should be made to collect outcomes after treatment discontinuation unless continued collection is inappropriate or consent is withdrawn.

The trial should distinguish:

• Discontinuation of the assigned intervention.
• Withdrawal from a particular assessment.
• Loss to follow-up.
• Withdrawal of consent for further data collection.
• Death.

These events have different meanings and should not all be labelled withdrawal. Reasons should be recorded by treatment group because missingness may be related to effectiveness, adverse events or treatment burden.

Intention-to-treat analysis

An intention-to-treat approach analyses participants according to their randomised groups, regardless of adherence, switching or treatment discontinuation. It preserves the comparison created by randomisation and often estimates the effect of assigning the intervention under trial conditions.

Intention-to-treat does not mean that missing outcomes can be ignored. An analysis that excludes participants without complete data may depart materially from the randomised comparison even when the remaining participants are analysed in their assigned groups.

Per-protocol and as-treated analyses can address different questions about adherence or treatment received, but they may be confounded because adherence and switching are not random. They should be prespecified, interpreted carefully and not treated as replacements for the primary randomised analysis without justification.

Estimating treatment effects

Trial results should report the effect size and its uncertainty rather than relying only on whether a statistical test crosses a significance threshold. The appropriate effect measure depends on the outcome and decision question.

For a binary outcome, the risk difference is:

$$ Risk\ difference = p_1 - p_0 $$

The relative risk is:

$$ Relative\ risk = \frac{p_1}{p_0} $$

where:

• (p_1) is the outcome risk in the experimental group.
• (p_0) is the outcome risk in the comparator group.

The same relative effect can produce different absolute effects in populations with different baseline risks. Decision making should therefore consider both relative and absolute effects.

For continuous outcomes, the analysis may report a mean difference or a standardised mean difference. Time-to-event outcomes commonly require methods that account for censoring and variation in follow-up.

Missing outcome data

Missing data can bias the estimated treatment effect when missingness is related to outcome, treatment group or post-randomisation events. The primary analysis should use methods consistent with explicit assumptions about why data are missing.

The trial should report:

• The amount of missing data for each outcome and group.
• Reasons for missingness when known.
• Characteristics of participants with and without observed outcomes.
• The statistical method used to handle missing data.
• Sensitivity analyses testing plausible alternative assumptions.

Simple methods such as complete-case analysis or carrying the last observation forward can be inappropriate. No statistical method can fully recover information that was never collected without relying on assumptions.

Adherence, switching and intercurrent events

Events occurring after randomisation can affect the meaning of the treatment effect. These include treatment discontinuation, switching, rescue therapy, competing events and death.

The estimand should state how each important event is handled. For example, a trial may estimate the effect of assignment regardless of discontinuation, the effect if all participants adhered, or the effect before a competing event occurs.

Different strategies answer different questions. The analysis should not switch between them according to which result appears most favourable.

Trial designs for different questions

Randomised trials can use several structures. The design should match the intervention, unit of delivery, expected treatment effect and risk of contamination.

• A parallel-group trial assigns participants to one intervention for the main study period.
• A crossover trial assigns participants to a sequence of interventions so that each person can contribute to more than one comparison.
• A cluster-randomised trial assigns groups such as clinics, schools or communities.
• A factorial trial evaluates more than one intervention within the same design.
• A stepped-wedge trial introduces an intervention to clusters in a randomised sequence over time.
• A pragmatic trial evaluates interventions under conditions intended to reflect routine practice.
• An adaptive trial permits prespecified modifications based on accumulating data while preserving valid inference.

Each design introduces particular analytical and operational requirements. A crossover design, for example, is inappropriate when treatment effects persist and cannot be separated by a suitable washout period.

Explanatory and pragmatic purposes

Explanatory trials test whether an intervention can work under controlled conditions, while pragmatic trials focus more directly on effectiveness in routine practice. Most trials fall somewhere between these purposes rather than fitting completely into one category.

Eligibility, treatment flexibility, follow-up intensity, outcome choice and adherence support influence where a trial sits. A pragmatic label does not compensate for poor randomisation, incomplete follow-up or unclear usual care.

Safety assessment

Trials should collect adverse events using definitions and methods appropriate to the intervention and population. The observation period should be long enough to identify important harms, and reporting intensity should be similar between groups.

Trials are often underpowered for rare or delayed harms. Safety interpretation may therefore require evidence from other trials, observational studies, registries and pharmacovigilance systems.

Benefits and harms should be reported together. A favourable primary outcome does not remove the need to examine serious or patient-important adverse effects.

Economic evaluation alongside a trial

A trial can collect patient-level resource use, costs and health outcomes for an economic evaluation. Randomisation supports an unbiased comparison of observed costs and outcomes during the trial period when missing data and analysis are handled appropriately.

Trial-based economic evaluation may include:

• Intervention and implementation costs.
• Healthcare and social-care resource use.
• Patient and caregiver costs.
• Productivity effects when relevant to the perspective.
• Health-related quality of life.
• Quality-adjusted life years.
• Incremental costs and outcomes.
• Uncertainty in joint cost and outcome differences.

The trial follow-up may be too short to capture long-term effects. A decision model can extrapolate beyond the trial, combine external evidence and compare additional strategies, but it adds assumptions that should be tested transparently.

A simplified example

Suppose 1,000 participants are randomised equally between a new intervention and usual care. The primary event occurs in 75 of 500 participants receiving the intervention and 100 of 500 receiving usual care.

The risks are:

$$ p_1 = \frac{75}{500} = 0.15 $$

$$ p_0 = \frac{100}{500} = 0.20 $$

The risk difference is:

$$ 0.15 - 0.20 = -0.05 $$

The intervention is associated with five fewer events per 100 participants during the trial period. The relative risk is:

$$ \frac{0.15}{0.20} = 0.75 $$

The estimated event risk is 25% lower relative to usual care. Interpretation should also consider confidence intervals, missing outcomes, adherence, adverse events and whether the trial population and comparator match the decision setting.

Internal and external validity

Internal validity concerns whether the observed comparison is credible for the participants studied. External validity concerns whether the result applies to other patients, settings and forms of care.

Restrictive eligibility, specialist centres, intensive follow-up and unusually high adherence may limit transferability. Broad eligibility and routine-care delivery may improve relevance but can create more variation in implementation.

A result should not be dismissed merely because the trial differs from practice. The important question is whether those differences are likely to modify the treatment effect or the feasibility of implementation.

Common misunderstandings

Randomised controlled trials provide strong protection against confounding when designed and conducted well, but the label alone does not establish high-quality evidence.

Common misunderstandings include:

• Randomisation does not guarantee balance in every measured characteristic, especially in small trials.
• Allocation concealment and blinding are not the same process.
• An open-label trial is not automatically invalid.
• A statistically significant result is not automatically clinically important.
• A non-significant result does not prove that interventions are equivalent.
• Intention-to-treat analysis does not justify ignoring missing data.
• A placebo is not always the relevant comparator for a healthcare decision.
• Trial evidence may be insufficient for rare harms, long-term outcomes or routine-practice costs.
• The term gold standard should not prevent examination of bias, relevance and ethical or practical limitations.

Interpreting trial evidence

A trial result should be interpreted in relation to the question, comparator, conduct, effect estimate, uncertainty and applicability. Randomisation supports causal inference for the comparison studied, but it does not answer questions the trial was not designed or powered to address.

A useful randomised controlled trial makes the allocation process, participant flow, outcomes, analysis and deviations transparent. Its contribution to a decision depends on both internal validity and the extent to which its population, interventions and setting reflect the decision that must be made.