How to Calculate Sample Size for a Randomized Controlled Trial

A randomized controlled trial assigns participants to a treatment arm and a control arm at random, then compares outcomes between them. Random assignment is what allows any observed difference to be attributed to the intervention itself, but that comparison is only trustworthy if each arm is large enough to reliably detect a real effect. This guide first explains what an RCT is and when it applies, then the general formula behind the calculation, then walks through how to apply it in AnalyZ Solutions.

01What an RCT is, and when it applies

An RCT is a study design in which participants, or sometimes whole groups such as clinics or villages, are assigned to a treatment or a control condition using a random process, such as a coin flip, a random number generator, or a lottery. Because assignment is random and not chosen by the participants, the researcher, or circumstance, the two arms should be similar to each other on average in every way except whether they received the intervention, both in ways that were measured and in ways that were not.

An RCT is a strong fit when three conditions hold together.

• The intervention can be withheld or delayed for some participants without causing harm. Random assignment requires a control arm that does not receive the intervention, or receives it later, or receives an alternative.
• Who receives the intervention can genuinely be randomised. This is often straightforward for a new programme with more eligible participants than available slots, and harder when local political, ethical, or logistical realities make random exclusion impractical.
• The outcome can be measured comparably in both arms. The same instrument, at the same time, in a way that is not itself influenced by which arm someone is in.

Why randomisation is often called the gold standard

The core problem in evaluating any intervention without randomisation is confounding: people or places that receive a programme often differ from those that do not, for reasons connected to the outcome itself. A programme that targets motivated communities, better resourced clinics, or households already on an upward trajectory will look effective even if it changed nothing, simply because of who ended up in the treatment group. Random assignment breaks this link. On average, across a large enough sample, the treatment and control arms start out balanced on every characteristic, measured or not, so any difference that emerges after the intervention can be attributed to the intervention itself rather than to pre-existing differences between the groups. This is what allows an RCT to support a causal claim, not just a correlation, and is why it is often described as the strongest available design for estimating impact.

Common pitfalls

• Randomisation that is not actually random. Assignment based on convenience, staff discretion, or a predictable pattern, such as alternating names on a list, undermines the balance that randomisation is meant to provide, even if it is described as random.
• Contamination between arms. If control participants can access the intervention informally, through spillover, sharing information, or geographic proximity to treatment participants, the true effect will be understated, since the control group is no longer a clean comparison.
• Attrition that differs between arms. If people drop out of the treatment and control arms for different reasons, or at different rates, the remaining sample may no longer be balanced, reintroducing the very problem randomisation was meant to solve. This is a different and more serious issue than attrition that happens at a similar, random rate in both arms.
• Assuming random assignment guarantees a large enough sample. Randomisation protects against bias, not against a trial being too small to detect the effect it was designed to find. That is a separate problem, solved by the sample size calculation itself.

02The general sample size formula

An RCT can compare either a proportion outcome (a rate, such as percentage employed) or a continuous outcome (a numeric score, such as average income). Each uses its own formula.

For a proportion outcome, comparing the rate in the control arm against the rate in the treatment arm:

For a continuous outcome, comparing the mean in each arm:

Each symbol plays a specific role, and each is a genuine judgment call rather than a fixed input.

• Z_1−α/2 (confidence level). How sure you want to be that a detected difference is real, rather than random noise, at 95% confidence this is 1.96. Set this based on how costly a false positive would be, a mistaken conclusion that the intervention worked when it did not.
• Z_1−β (power). How likely you want to be to actually detect the effect, if it is really there, at 80% power this is approximately 0.84. Set this based on how costly it would be to miss a real effect, for example if a funding decision hinges on the result.
• p₁ and p₂ (proportion outcome), or σ and Δ (continuous outcome). These together define the minimum effect the trial is built to detect. Set p₁ or σ from baseline data, a prior evaluation, or a pilot. Set p₂ or Δ based on the smallest effect that would be considered programmatically meaningful, not the effect you hope for in an optimistic scenario.

How to set confidence level and power in practice

95% confidence and 80% power are conventional defaults, appropriate for most trials with no specific reason to depart from them. Two situations commonly justify moving away from these defaults.

• Raise power to 90% when the trial result will directly determine whether an intervention is scaled, continued, or defunded, since missing a real effect in that situation has serious downstream consequences.
• Tighten confidence below 0.05 when a false positive would lead to a costly, hard to reverse decision, such as a national policy recommendation based on the trial.

Relaxing either value below the conventional default, rather than raising it, is a much less common and generally harder to justify choice, since it directly increases the chance of either a false positive or a missed effect, whichever value is relaxed.

Setting the minimum detectable effect

The gap between p₁ and p₂, or the value of Δ, is the single input most likely to be set unrealistically in practice. It should reflect the smallest effect that would still be considered a meaningful, worthwhile result for the intervention being tested, not the effect the programme team hopes to see in a best case scenario. A trial sized around an optimistic effect that does not materialise will very likely be underpowered to detect the real, smaller effect the intervention actually produces. Where possible, base this figure on effects found in similar interventions in comparable settings, published evaluation literature, or a pilot study, rather than an aspirational target.

One-tailed or two-tailed

The formulas above use Z_1−α/2, the two-tailed critical value, appropriate when testing for a difference in either direction. A one-tailed test, appropriate only when a change in one specific direction is the sole interest, uses Z_1−α instead, a smaller value that produces a smaller required sample for the same nominal confidence level. Two-tailed is the safer, more conventional default, and is expected by most funders and ethics reviewers unless there is a specific, defensible reason a change in the unexpected direction genuinely does not need to be detected.

Accounting for cluster randomisation

If whole groups, such as clinics, schools, or villages, are randomised to arms rather than individuals, a design effect must be applied. It defaults to 1, meaning no clustering effect, and is always editable. Skipping this adjustment for a cluster-randomised trial will understate the required sample, often substantially, because outcomes within the same cluster tend to be correlated. See the dedicated guide on Design Effect and ICC for how to set this correctly.

The RCT tool in the Sampling module applies both formulas above automatically, along with attrition and design effect adjustments.

1. Choose your outcome type. Select Proportion outcome or Continuous (mean) outcome. This determines which formula and which inputs follow.
2. Set confidence and power. Enter both as numbers. Defaults are 95% confidence and 80% power.
3. Enter the effect you want to detect. For a proportion outcome, enter the expected rate in the control group and the expected rate in the treatment group. For a continuous outcome, enter the expected standard deviation and the expected difference between arms.
4. Set expected attrition. This inflates the per-arm recruitment target so the analysed sample still meets the statistical minimum after losses to follow-up.
5. Choose one-tailed or two-tailed. Two-tailed is selected by default and is appropriate for almost all trials.
6. Set a design effect, if cluster-randomised. If whole groups, such as clinics or schools, are randomised rather than individuals, enter a design effect directly or calculate one from an intraclass correlation and average cluster size. It defaults to 1, meaning no clustering effect, and is always editable.

03Worked example

Suppose you are evaluating a job readiness training programme. Currently 40% of a comparable population finds employment within six months. You expect the programme to lift this to 55%. You want 80% power at 95% confidence, two-tailed, and expect 15% attrition by endline.

04Common mistakes to avoid

• Powering for every outcome measured, not the primary one. Power the trial for its pre-specified primary outcome. Reporting additional outcomes is fine, but powering for all of them inflates the sample and invites multiple comparison problems.
• Randomising clusters but using the individual-level formula. If clinics, schools, or villages are assigned to arms rather than individuals, the design effect must be applied, or the trial will likely be underpowered.
• Choosing an unrealistically large expected effect. Sizing a trial around an optimistic effect that does not materialise is a common way evaluations end up underpowered in practice.
• Treating randomisation as a substitute for adequate sample size. A correctly randomised trial that is too small can still fail to detect a real effect. Randomisation addresses bias, not statistical power.