Grant writing

Sample size and analysis plan sections in a clinical research grant

A worked sample size justification, where the effect size should come from, how to allow for attrition, and an analysis plan table matched to each aim.

Editverse Medical editorial deskPublished 10 November 2026Guideline versions checked November 2026

Key points

A sample size justification names seven things: the primary outcome, the comparison, the target effect and its source, the variability and its source, alpha, power, and the allowance for loss to follow-up.
The target effect should be the smallest difference that would change practice, supported by published evidence. A pilot study's observed effect is a weak basis.
Inflate for attrition by dividing by the proportion expected to remain, not by adding a percentage.
For an NIH clinical trial, the Statistical Design and Power attachment must give the number of subjects, the expected effect size, the power and the statistical methods for each outcome measure listed on the form.
The analysis plan is easiest to review as a table with one row per aim: estimand, analysis population, model, handling of missing data, and multiplicity.

What reviewers are checking

Reviewers of a clinical research grant read the sample size and analysis sections to answer one question: if this study is funded and completed, will its result be believed? Under NIH's simplified review framework that judgement sits in Factor 2, Rigor and Feasibility, one of the two scored factors.¹ The Research Strategy instructions ask applicants to describe the experimental design and methods and how they will produce unbiased results, including how data will be collected, analysed and interpreted, and to explain how relevant biological variables such as sex are factored into designs and analyses.²

For studies that meet the NIH definition of a clinical trial there is a second, more exact requirement. Field 4.3 of the PHS Human Subjects and Clinical Trials Information form, Statistical Design and Power, asks for the number of subjects expected to be enrolled, the expected effect size, the power, and the statistical methods to be used with respect to each outcome measure listed in field 4.2. Applicants must show that the methods for sample size and analysis suit the way participants are assigned and interventions delivered, and NIH notes that trials which randomise groups, or deliver interventions to groups, need special methods.³ The same instructions say not to duplicate information between the Research Strategy and the form. In practice the Research Strategy carries the reasoning and the attachment carries the full specification.

The seven elements of a justification

What a sample size justification must state
#	Element	What to write	Common fault
1	Primary outcome	One outcome, its measurement method and its time point.	Several "primary" outcomes with no adjustment.
2	Comparison and design	Groups compared, allocation ratio, superiority or non-inferiority, unit of randomisation.	Individual-level calculation for a cluster-randomised design.
3	Target effect and source	The difference the study is designed to detect, and why that size matters.	Effect chosen to fit the budget.
4	Variability and source	Standard deviation, control-group event rate or other nuisance parameter, with a citation or dataset.	Value stated without a source.
5	Type I error	Alpha, one- or two-sided, and any split across outcomes or interim looks.	Interim analyses planned but alpha unadjusted.
6	Power	Target power, and the test or model on which the calculation is based.	Calculation based on a different test from the planned analysis.
7	Attrition and final number	Expected loss, its source, the inflated number to randomise, and the software used.	No allowance, or allowance added the wrong way.

The SPIRIT 2025 statement for trial protocols and the CONSORT 2025 statement for trial reports both ask for the sample size determination to be reported, so a justification written to this standard can be carried straight into the protocol and, later, the paper.¹⁰¹¹

Where the effect size should come from

The target effect is the number reviewers question most. There are four usual sources, in rough order of strength.

A minimal clinically important difference established for the outcome in the population being studied. This answers the question a funder cares about: would a difference of this size change what clinicians do?
Effects seen in earlier trials or a meta-analysis of comparable interventions, used as a guide to what is plausible, and quoted with their confidence intervals.
A difference agreed with clinicians and patients as worth the cost and burden of the intervention, documented as part of the application's stakeholder work.
Pilot data. A pilot is good evidence for feasibility, for the standard deviation and for the control-group rate. Its observed effect is imprecise, because small studies give wide intervals, and powering the main study on it is a frequent criticism.

The strongest paragraphs combine two sources: a target effect justified as clinically important, shown to be plausible against earlier trials. They then give the variability from the largest relevant dataset available, which is where pilot or registry data earn their place.

Worked example: a justification paragraph

The example is illustrative. The trial, values and sources are invented, and any real calculation should be rerun by the study statistician in validated software.

Illustrative text

The primary outcome is change in HbA1c from baseline to 26 weeks. The trial is designed to detect a between-group difference of 0.4 percentage points, the smallest difference our clinical advisory group and the published literature regard as sufficient to alter treatment. We assume a standard deviation of change of 1.0 percentage point, taken from the control arm of our 180-participant feasibility study and consistent with two earlier trials in this population. With a two-sided alpha of 0.05 and 90 percent power, a two-sample comparison of means requires 132 participants per group. We expect 15 percent of participants to have no 26-week measurement, based on the feasibility study (13 percent) and allowing a margin. We will therefore randomise 156 participants per group, 312 in total, in a 1:1 ratio. The primary analysis will adjust for baseline HbA1c, which is expected to increase power above the level calculated here.

The arithmetic behind the paragraph is shown so that it can be checked.

Calculation steps for the illustrative example
Step	Working	Result
Standardised difference	0.4 divided by 1.0	0.40
Normal deviates	1.960 for two-sided alpha 0.05, plus 1.282 for 90 percent power	3.242
Per group, before attrition	2 multiplied by 3.242 squared, divided by 0.40 squared: 2 × 10.51 ÷ 0.16	131.4, rounded up to 132
Allowance for 15 percent loss	132 divided by 0.85	155.3, rounded up to 156
Total to randomise	156 multiplied by 2	312

Two details deserve attention. The figure of 132 comes from the normal approximation; software using the t distribution will return a value one or two higher, and the application should quote whichever method the statistician used. And the attrition step divides by 0.85. Multiplying 132 by 1.15 gives 152, which would leave the trial short of its target if 15 percent were lost.

Designs that change the calculation

Cluster randomisation. Clinics, wards or villages are randomised, and outcomes within a cluster are correlated. The individual-level number is multiplied by a design effect that depends on cluster size and the intracluster correlation, and both need a source. This is the case NIH singles out as needing special methods.³
Binary and time-to-event outcomes. The inputs are the control-group event rate and the target risk difference or hazard ratio. For time-to-event outcomes it is the number of events, not participants, that drives power, so accrual and follow-up time must be stated.
Non-inferiority. The margin has to be justified clinically and statistically, and the choice of analysis population matters more than in a superiority trial.
More than one primary comparison. Several outcomes, doses, populations or interim analyses each create multiplicity. The control strategy belongs in the sample size paragraph because it changes alpha.⁹
Observational and prediction studies. The justification is framed around the precision of the estimate, or the number of events available for the model, with the fixed size of the dataset stated openly.

The analysis plan, matched to each aim

ICH E9 sets the general expectations for trial analysis: pre-specification, defined analysis sets, and planned handling of multiplicity and missing data. The E9(R1) addendum adds the estimand, which defines what each objective is estimating through five attributes: population, treatment, variable, intercurrent events with the strategy for each, and population-level summary.⁴⁵⁶ A grant does not need a full statistical analysis plan, which runs to 55 recommended items in the published guidance on content,⁷ but it should show that the applicants know what will go in one.

A table does this in the least space. The rows below continue the illustrative trial.

Illustrative analysis plan by aim (invented trial)
Aim	Estimand in brief	Population	Primary analysis	Missing data	Multiplicity
1. Effect on glycaemic control at 26 weeks	Mean difference in HbA1c change, regardless of adherence or rescue medication (treatment-policy strategy)	All randomised	Analysis of covariance with treatment, baseline HbA1c and site	Multiple imputation under missing at random; tipping-point sensitivity analysis	Single primary test at two-sided 0.05
2. Effect on severe hypoglycaemia	Rate ratio for events over 26 weeks	All randomised who received at least one dose	Negative binomial regression with follow-up time as offset	Follow-up time handles early withdrawal; sensitivity analysis for informative dropout	Key secondary; tested only if Aim 1 is significant
3. Effect modification by baseline renal function	Difference in treatment effect between prespecified subgroups	All randomised	Treatment-by-subgroup interaction term in the Aim 1 model	As Aim 1	Exploratory; reported with interaction estimate and interval

Three habits make this table credible. Each analysis population is defined, not just named. Missing data are handled with a stated assumption and a sensitivity analysis, since no single method is valid in all circumstances and prevention through design comes first.⁸ Subgroup questions are tested with interaction terms and labelled as exploratory unless the study is powered for them.

Where each piece goes in an NIH application

Placement of statistical content
Location	Content
Research Strategy, Approach	Design rationale, the justification paragraph for the primary outcome, the aim-by-aim table, treatment of sex as a biological variable, and the main threats to validity with the planned response.
Human Subjects form, 4.2 Outcome Measures	Each primary, secondary and other outcome with its time frame. Names must match those used in the Research Strategy.
Human Subjects form, 4.3 Statistical Design and Power	For each listed outcome: number enrolled, expected effect size, power and method. This is where secondary outcomes get their power statements.
Data and Safety Monitoring Plan	Interim analyses and stopping rules, if any, consistent with the alpha stated in the sample size paragraph.
Budget justification	Statistician effort that matches the complexity of the plan.

Inconsistency between these locations is the most avoidable weakness. The number to be enrolled should be identical in the Research Strategy, the Statistical Design and Power attachment, the recruitment plan and the inclusion enrollment table.

What a statistician needs from the investigator

You provide: Aims and hypotheses, the primary outcome and time point, the design, the smallest difference that would matter clinically, any pilot or registry data, and expected recruitment and dropout.
What is done: Parameters sourced and referenced; calculation run and re-checked against the stated assumptions; justification paragraph drafted for the protocol or grant.
You receive: A calculation report with the assumptions and software output, the grant-ready paragraph, and a design memo.

Editverse Medical provides this through its sample size, power and study design service, on its own or as part of a research grant proposal. The statisticians' wider work is described on the statistical interpretation page.

Is 80 percent power enough for a grant application?

Eighty percent is widely used and accepted. Ninety percent halves the chance of missing a real effect and is often expected for a definitive trial. State the figure, give the reason, and show in a short table how power changes if the effect or the standard deviation differs from the assumption.

Can I base the sample size on my pilot study's result?

Use the pilot for recruitment and retention rates and for the variability of the outcome. Avoid using its observed treatment effect as the target, because small studies estimate effects imprecisely. Anchor the target to a clinically important difference instead.

Do secondary outcomes need power calculations?

For an NIH clinical trial, the Statistical Design and Power attachment asks for expected effect size, power and methods with respect to each outcome measure listed on the form. A brief statement of the power available for each key secondary outcome at the planned sample size meets this.

What if the affordable sample is smaller than the calculated one?

Say so, and redesign: a more precise outcome, adjustment for baseline, a longer accrual period, more sites, or a narrower question. Changing the target effect until the number fits the budget is visible to reviewers and weakens the application.

References

National Institutes of Health. Simplified Peer Review Framework. Page last updated 28 April 2026. grants.nih.gov
National Institutes of Health. G.400: PHS 398 Research Plan Form. SF424 (R&R) Application Guide, FORMS-I. grants.nih.gov
National Institutes of Health. G.500: PHS Human Subjects and Clinical Trials Information. SF424 (R&R) Application Guide, FORMS-I. grants.nih.gov
International Council for Harmonisation. ICH Harmonised Tripartite Guideline E9: Statistical Principles for Clinical Trials. 1998. database.ich.org
International Council for Harmonisation. ICH Harmonised Guideline E9(R1): Addendum on Estimands and Sensitivity Analysis in Clinical Trials. Step 4, 2019. database.ich.org
Kahan BC, Hindley J, Edwards M, Cro S, Morris TP. The estimands framework: a primer on the ICH E9(R1) addendum. BMJ. 2024;384:e076316. PMID 38262663 · DOI
Gamble C, Krishan A, Stocken D, Lewis S, Juszczak E, Doré C, et al. Guidelines for the Content of Statistical Analysis Plans in Clinical Trials. JAMA. 2017;318(23):2337-2343. PMID 29260229 · DOI
Little RJ, D'Agostino R, Cohen ML, Dickersin K, Emerson SS, Farrar JT, et al. The prevention and treatment of missing data in clinical trials. N Engl J Med. 2012;367(14):1355-60. PMID 23034025 · DOI
Dmitrienko A, D'Agostino RB Sr. Multiplicity Considerations in Clinical Trials. N Engl J Med. 2018;378(22):2115-2122. PMID 29847757 · DOI
Chan AW, Boutron I, Hopewell S, Moher D, Schulz KF, Collins GS, et al. SPIRIT 2025 statement: updated guideline for protocols of randomised trials. BMJ. 2025;389:e081477. PMID 40294953 · DOI
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. PMID 40228833 · DOI

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