Adjustments to Sample Size

Overview

A basic sample-size formula commonly assumes:

• independent observations;
• simple random sampling;
• complete outcome data;
• equal allocation;
• one primary comparison;
• the anticipated effect and variability are correct; and
• every recruited participant contributes to the primary analysis.

Real studies often depart from these assumptions.

The base calculation may therefore require adjustment for:

• nonresponse or attrition;
• cluster sampling or cluster randomisation;
• unequal cluster sizes;
• unequal group allocation;
• finite populations;
• non-adherence or treatment switching;
• multiple primary claims;
• important subgroup objectives;
• missing specimens or indeterminate results;
• whole-cluster loss; and
• uncertainty in planning inputs.

Each adjustment should correspond to a specific loss of information or design requirement. Inflating the sample repeatedly without identifying what each factor represents can double count the same problem.

Why this matters

Three sample-size numbers may be needed:

1. analysable sample: observations needed in the primary analysis;
2. recruitment target: participants or clusters to enrol so that the analysable sample remains after loss; and
3. number approached or screened: people who must be invited to achieve the recruitment target.

These quantities are not interchangeable.

For example, a study needing 400 analysable participants may require 445 recruited participants if 10% are expected to lack the primary outcome. If only half of eligible people agree to participate, approximately 890 may need to be invited.

A protocol that reports only “sample size = 400” leaves the operational plan unclear.

Adjusting for individual attrition or nonresponse

Let:

• $n_A$ be the required analysable sample;
• $L$ be the anticipated loss proportion; and
• $R=1-L$ be the anticipated retention or response proportion.

If 244 analysable participants are needed and 10% are expected to be missing:

$$n_{\mathrm{recruit}} = \frac{244}{0.90} = 271.11$$

Round upward to 272 participants before considering clustering.

Why adding 10% is insufficient

Adding 10% gives:

$$244\times1.10=268.4$$

If 10% of 269 recruited participants are lost, the expected analysable number is:

$$269\times0.90=242.1$$

This is below 244.

The difference is modest at 10% loss but increases as loss becomes larger.

Distinguish types of loss

Different losses may occur at different stages:

• ineligible after screening;
• refuses consent;
• randomised but never starts treatment;
• stops treatment but remains followed;
• misses the primary outcome;
• specimen unsuitable;
• record cannot be linked; or
• cluster withdraws.

Only losses that remove information needed for the primary analysis should inflate the analysable requirement. Treatment discontinuation should not automatically be equated with missing outcome data.

Cluster design effect

Participants within the same clinic, school, household or community tend to be more similar than participants from different clusters.

The intracluster correlation coefficient, abbreviated ICC, measures the correlation between outcomes from two randomly selected individuals in the same cluster under a specified model.

For equal cluster size $m$, a common design effect is:

The cluster-adjusted analysable sample is approximately:

$$n_{\mathrm{cluster}} = n_{\mathrm{individual}}\times DE$$

For $m=20$ and $\rho=0.03$:

$$DE=1+(20-1)(0.03)=1.57$$

Applying this to 244 individually independent observations:

$$244\times1.57=383.08$$

Round upward to at least 384 analysable participant observations.

However, participants are recruited in whole clusters. With 20 analysable participants per clinic:

$$384/20=19.2$$

At least 20 clinics are required, giving 400 planned analysable participant observations.

Worked example

Unequal cluster sizes

The simple design effect assumes equal cluster sizes. In practice, clinic sizes vary.

Unequal sizes generally reduce efficiency because large clusters contribute increasingly redundant information when the ICC is positive. Kerry and Bland showed that ignoring size variation can lead to underestimation of the required sample [1].

An approximate correction sometimes uses the coefficient of variation of cluster size, but the appropriate method depends on:

• number of clusters;
• cluster-size distribution;
• analysis model;
• allocation;
• outcome type; and
• whether cluster size is informative.

Dedicated cluster-trial software or simulation is preferable when sizes differ substantially.

Sensitivity to the intracluster correlation

simulated data

Table 1. Design effect for 20 analysable participants per clinic

ICC	Design effect	Independent base of 244 after inflation
0.01	1.19	291
0.03	1.57	384
0.05	1.95	476
0.10	2.90	708

Note: Values are rounded upward before cluster rounding. ICC = intracluster correlation coefficient.

(Calculations for the sensitivity-table design effects and inflated samples are not shown here; they use the formula and base sample presented above.)

Small ICCs can have large effects when clusters contain many participants.

Number of clusters

Cluster-randomised studies require enough clusters for:

• treatment-effect estimation;
• valid standard-error estimation;
• covariate adjustment;
• balance across arms; and
• resilience to cluster withdrawal.

The individual-level design-effect approximation does not guarantee that the number of clusters is sufficient.

With few clusters, small-sample corrections and cluster-level methods may be required. The number of clusters should be determined using a cluster-aware calculation, not only by dividing an inflated participant total by mean cluster size.

Whole-cluster loss

If 20 analysable clinics are required and 10% whole-cluster loss is anticipated:

$$20/0.90=22.22$$

At least 23 clinics should be recruited.

Whole-cluster and individual-level loss are separate. If both are plausible, each should be represented without applying the same loss twice.

Unequal allocation

For a two-group independent comparison with similar variances, equal allocation is usually most efficient.

At allocation ratio $r=n_1/n_0$, an approximate total-sample inflation relative to 1:1 is:

$$IF_{\mathrm{alloc}} = \frac{(1+r)^2}{4r}$$

At 2:1 allocation, the factor is 1.125.

Unequal allocation may still be justified by:

• intervention cost;
• limited control availability;
• safety information;
• recruitment preference;
• expected variance differences; or
• a shared control in a multi-arm trial.

The calculation should incorporate the actual allocation directly.

Finite-population correction

When sampling without replacement from a genuinely finite target population, a finite-population correction may reduce the required sample.

It should be applied before nonresponse inflation and only when inference is restricted to that finite population.

It does not apply merely because a current register has a finite number of entries if the scientific target is a continuing population.

Multiplicity and several primary objectives

If success requires more than one confirmatory claim, the type I error may need to be controlled across them.

Examples include:

• two co-primary outcomes;
• several treatment arms versus one control;
• multiple doses;
• several primary time points; and
• confirmatory subgroup claims.

A smaller significance level generally increases sample size.

If success requires both co-primary endpoints to be significant, power depends on their joint distribution. A simple Bonferroni adjustment may not be optimal.

Subgroup objectives

A study powered for an overall effect is rarely powered automatically for:

• separate effects in men and women;
• individual age groups;
• treatment-by-biomarker interaction; or
• rare disease categories.

Testing effect modification requires an interaction effect and usually far more information than detecting an overall treatment effect.

Recruiting enough participants for every subgroup should be justified by genuine primary objectives rather than an indiscriminate desire to “allow subgroup analysis”.

Pilot and feasibility studies

Pilot studies should be sized for their own objectives.

Examples include precision for:

• recruitment rate;
• retention rate;
• process adherence;
• variance;
• ICC; and
• feasibility progression criteria.

Small pilot estimates of SD or ICC can be unstable. Teare and colleagues demonstrated that pilot sample size should be selected according to the parameter requiring estimation rather than a fixed percentage of the main study [2].

A pilot should not be called adequately powered for treatment efficacy unless it has been designed as a definitive efficacy study. Comprehensive cluster-trial guidance also stresses that participant numbers, cluster numbers and analysis assumptions must be planned together [3], [4].

Losses after randomisation can erode the intended information and should be prevented and reported, not merely inflated away [5]. External pilot sizing may also be chosen to improve estimation of the main study’s nuisance parameters rather than by an arbitrary rule [6].

Combining adjustments safely

Blinded sample-size re-estimation MMed extension

A blinded internal pilot may update nuisance parameters such as:

• pooled variance;
• pooled event rate;
• overall recruitment;
• aggregate event frequency; or
• ICC.

Because treatment-group effects remain masked, blinded re-estimation may preserve trial integrity more readily than unblinded adaptation.

The procedure, timing, maximum sample and type I error implications should be prespecified. Re-estimation is not a substitute for realistic initial planning.

Suggested reporting

Common mistakes

Knowledge check

Why is a 10% loss adjustment calculated by dividing by 0.90?

Answer and reasoning

Only 90% of recruited participants are expected to remain analysable. Division determines how many must be recruited to retain the required information after loss.

What does the cluster design effect represent?

Answer and reasoning

It is the approximate factor by which variance, and therefore sample requirement, increases because observations within the same cluster are correlated.

Why are whole-cluster loss and individual missingness adjusted separately?

Answer and reasoning

They occur at different levels. Losing one clinic removes all its participants and an independent cluster, whereas individual missingness removes only selected participant outcomes.

Why can an ICC of 0.03 matter substantially?

Answer and reasoning

The design effect contains $(m-1)\rho$. Even a small ICC accumulates when many participants are recruited within each cluster.

Does adequate overall power imply adequate power for an interaction?

Answer and reasoning

No. Interaction effects are usually estimated less precisely and may be smaller than the overall effect. They require their own planning assumptions and calculation.

Key take-home messages

References

1. Kerry SM, Bland JM. Unequal cluster sizes for trials in English and Welsh general practice: implications for sample size calculations. Stat Med. 2001;20(3):377–390. https://doi.org/10.1002/1097-0258(20010215)20:3%3C377::AID-SIM799%3E3.0.CO;2-N
2. Teare MD, Dimairo M, Shephard N, Hayman A, Whitehead A, Walters SJ. Sample size requirements to estimate key design parameters from external pilot randomised controlled trials: a simulation study. Trials. 2014;15:264. https://doi.org/10.1186/1745-6215-15-264
3. Eldridge SM, Kerry S. A practical guide to cluster randomised trials in health services research. Chichester: Wiley; 2012. https://doi.org/10.1002/9781119966241
4. Donner A, Klar N. Design and analysis of cluster randomization trials in health research. London: Arnold; 2000.
5. Schulz KF, Grimes DA. Sample size slippages in randomised trials: exclusions and the lost and wayward. Lancet. 2002;359(9308):781–785. https://doi.org/10.1016/S0140-6736(02)07882-0
6. Whitehead AL, Julious SA, Cooper CL, Campbell MJ. Estimating the sample size for a pilot randomised trial to minimise the overall trial sample size for the external pilot and main trial for a continuous outcome variable. Stat Methods Med Res. 2016;25(3):1057–1073. https://doi.org/10.1177/0962280215588241