How to Report an A Priori Power Analysis in APA 7

Reviewer 2 asks for it in five words: “please justify your sample size”. And you have 96 participants who cost fourteen months of recruitment across two mental health services, G*Power open on the screen, and the temptation to type in the effect you actually got just to see what power comes back. That road ends badly, because the number it returns says nothing the p value has not already said two columns earlier. Here is what you do declare, in what order and in what words, and what to write when the sample is closed and there is nothing left to plan. If what you need is the calculation before you start, that step lives in how to calculate the sample size for a thesis.

The six things you declare

A properly reported a priori power analysis fits in two sentences, and those two sentences have to carry six things: the exact test, α and the number of tails, the target power, the effect size and its source, the resulting N and the software with its version. Miss any one of the six and the reader cannot rerun the calculation, and a calculation nobody can rerun is not a justification: it is a number.

“An ANOVA was conducted” is not a test. G*Power returns different answers for the main effect, for the interaction and for a contrast between two levels of the same design, so the effect you are going to test gets named in full: “the group × time interaction of a 2 × 3 mixed ANOVA”. This is the mistake that most often turns a correct calculation into a useless one: the sample is planned for the main effect of group while the paper's hypothesis is the interaction, which almost always needs more people. An interaction half the size of the main effect multiplies the required sample by four.

α and the tails travel together. The standard is α = .05, two-tailed, and a one-tailed test buys you a smaller sample by giving up any chance of detecting an effect in the opposite direction: defensible when the direction was preregistered, cosmetic when it appears exactly at the point where two-tailed did not reach. The conventional target is power = .80, which comes from Cohen (1988) as a reasonable settlement when a Type I error is treated as roughly four times more serious than a Type II error, not from a law of nature: for an expensive trial or a study nobody will replicate, .90 or .95 defend themselves. Neither α nor power carries a leading zero, because both are probabilities.

The N the software returns is reported whole and per group, and with it the actual power, which almost never lands exactly on what you asked for because people come in integers: asking for .80 with d = 0.50 returns 128 participants, 64 per group, and actual power of .8015, written up as .80. The software is cited with its version and reference (G*Power 3.1.9.7; Faul et al., 2007), because formulae have changed between releases. And if your design loses people, the N from the calculation is the one that has to remain, not the one you recruit: with 15% expected attrition, 128 at the end means 152 at the start, 76 per group, and that goes in the same sentence.

Where the effect size comes from, which is what actually gets reviewed

The effect size is the only input that convention does not fix for you, and it moves the sample brutally. With α = .05 two-tailed and power .80, an independent-samples t test asks for 128 participants at d = 0.50 and 352 at d = 0.30. A correlation asks for 84 at r = .30 and 194 at r = .20. Changing that box by a tenth does not fine-tune the calculation: it rewrites it. Which is why a competent reviewer does not look at your N, they look at where the effect came from.

The underlying conceptual error is typing in “the effect I expect to find”. What goes in is the smallest effect you would not want to miss, and that is hardly ever the same number. If a three-point drop on the BDI-II is the least a clinician would call a change worth having, your calculation anchors there and not on the d = 0.80 from the most enthusiastic study in the literature. That anchor has a name, the smallest effect size of interest, and it turns a statistical decision into a clinical one, which is what it was all along.

A meta-analysis of the specific effect is the best source available when one exists, with one caveat: the pooled estimate is inflated by publication bias, so you use the lower bound of its interval rather than the point estimate. A single previous study is a poor source; if it was published because it reached significance, its d is a ceiling, not an average. Your own pilot is the worst of the lot: with 20 people per group, an observed d of 0.40 carries a confidence interval running from −0.23 to 1.03, and planning on the midpoint of that range is planning on noise. Cohen's (1988) benchmarks are the last legitimate resort, and they get labeled as what they are.

Whatever the source, it gets named in the same sentence as the number. “d = 0.50” says nothing; “d = 0.50, the lower bound of the interval from the most recent meta-analysis of brief anxiety interventions” says where it came from, can be argued with, and can be reproduced. When there genuinely is nothing prior, the honest sentence is “in the absence of prior estimates, a medium effect was assumed following Cohen's (1988) conventions”; written that way it reads as an assumption, and written as “a medium effect was expected” it reads as data, which it is not. If the typical effect in your field sits around 0.30, planning for 0.50 is not optimism: it is designing a study whose non-significant result you could have predicted before recruiting anyone.

The Method paragraph, in full

Here it is with all six pieces inside and not a word to spare: “Sample size was determined a priori using G*Power 3.1.9.7 (Faul et al., 2007). To detect a between-groups difference of d = 0.50, the lower bound of the confidence interval from the most recent meta-analysis of brief anxiety interventions, with a two-tailed independent-samples t test, α = .05 and power of .80, 128 participants are required (64 per group; actual power = .80). Anticipating 15% attrition, 152 participants were recruited, 76 per condition.”

It belongs in the Method, inside Participants or under its own heading (“Sample size determination”), and in the past tense, because it describes a decision you already made. For a different design only two pieces change, the effect being tested and the metric it is expressed in: “to detect the group × time interaction (f = 0.25) of a 2 × 3 mixed ANOVA, assuming a correlation of .50 among repeated measures”, or “to detect an increment in R² corresponding to f² = 0.15 for one tested predictor out of four in the model”. The skeleton is identical in every case.

If you preregistered, the sentence points to the registration and its date, and the number in the registration has to match the number in the paper. When it does not, you say why: a site dropped out, recruitment closed in June, 118 came in instead of 152. An explained mismatch is an ordinary setback; a silent one is what makes a reviewer start reading the rest of your Method with a magnifying glass.

What does not pass is the filler sentence that shows up in half of all manuscripts: “G*Power was used to calculate the required sample size”. That is not a power analysis, it is an acknowledgment that the software exists. Giving the N without the effect, or the effect without its source, does not pass either. And if the Method declares 128 while the Results analyze 96, the power analysis has stopped justifying anything and you owe the reader an account of what happened in between.

Observed power tells you nothing

Post hoc power, also called observed power, is computed after the analysis using the effect size you obtained. SPSS offers it behind a tick box (“observed power”), which is why it shows up in so many ANOVA tables. The problem is not that it is hard to interpret: it is that it carries no new information. With the same N and the same test, observed power is a decreasing function of the p value, so knowing it is the same as knowing the p you are already looking at two columns along.

Numbers make the point better than definitions do. In a two-tailed z test, p = .05 corresponds exactly to observed power of .50, and from there the larger the p, the smaller the observed power, always. A t(94) = 1.62, p = .108, d = 0.33 returns observed power of about .36. It does not return that because your study had some specific problem, it returns it because p was .108. Any non-significant result gives observed power below .50 as a matter of arithmetic, which is why “the result was not significant because observed power was low” is circular: it says the result was not significant because the result was not significant. Hoenig and Heisey (2001) called it the power approach paradox.

When a reviewer asks for post hoc power, that is almost never what they want. They want to know whether your null result is an absence of effect or an absence of data, which is a fair question, and there are three ways of answering it that do inform: the confidence interval on the effect, which already contains all the uncertainty; a sensitivity analysis, which states the smallest effect you could have detected; and, if your hypothesis was one of absence, an equivalence test. The long version, with the reviewer reply included, is in post hoc statistical power analysis.

If the reviewer insists, there is no need for a fight. Give them the sensitivity analysis and the interval on the effect in the same paragraph, plus one sentence explaining why observed power would add nothing: “observed power is a monotone transformation of the p value (Hoenig & Heisey, 2001); the smallest detectable effect and the confidence interval around the observed effect are reported instead”. In my experience that sentence is accepted far more often than it is argued with.

If the sample is already collected: sensitivity analysis

A sensitivity analysis is the same calculation with the unknown moved: you fix the N you have, α and power, and solve for the effect size. With 96 participants, 48 per group, α = .05 two-tailed and power .80, the smallest detectable effect is d = 0.58. That is a sentence with content: it says effects below 0.58 had better than a one-in-five chance of slipping past your study, and it says so without using the result you obtained.

The wording is short: “Given the final sample size (N = 96), a sensitivity analysis indicated that the study had .80 power to detect effects of d ≥ 0.58 (α = .05, two-tailed)”. Then comes the uncomfortable part, the one that separates an honest sensitivity analysis from a decorative one: is 0.58 a plausible effect in your field? If the literature in your area lives between 0.20 and 0.35, your study was built to detect something that probably does not exist, and saying so before the reviewer does saves you a whole round.

With secondary data, clinical registries or a cohort that already existed, you did not choose the size and there is nothing to plan: the resource constraint is declared for what it is. Lakens (2022) recognizes it as a legitimate justification as long as it comes with the part you can state, which is how far the available sample reached. “Sample size was determined by the number of clinical records available in the study period; a sensitivity analysis indicates that...” is a sentence that passes. “It was estimated that 240 patients would suffice”, written after counting 240 patients, is not.

For the usual clinical designs, two groups, pre-post measures or event rates, the clinical sample size calculator runs all three directions of the calculation (N, power and smallest detectable effect) with nothing to install. And if the doubt is what the d you are typing into the box actually means, the benchmarks are unpacked in interpreting Cohen's d.

Three designs where G*Power falls short, and five mistakes

In repeated measures there is one box that decides the answer and that almost nobody reports: the correlation among repeated measures. Moving from ρ = .50 to ρ = 0 exactly doubles the sample G*Power asks for on the interaction, because the required N is proportional to 1 − ρ. The nonsphericity correction does the same job in the other direction. Both are your assumptions rather than outputs of the software, so both get written down: “assuming a correlation of .50 among repeated measures and ε = 1”.

If your data are nested, pupils in classrooms, patients within therapists, sessions within participant, the standard calculation comes out short and G*Power will not fix it. The correction runs through the design effect, 1 + (m − 1) × ICC, where m is the average cluster size: with 20 pupils per classroom and an ICC of .05, the factor is 1.95, which means nearly twice the participants for the same power. And an ICC of .05 in educational or clinical variables is modest, not extreme.

Indirect effects do not fit either, because the product of two coefficients is not normally distributed and there is no closed-form solution. They are handled by Monte Carlo simulation, and the figures are startling: with both paths medium, around 80 people will do, but if one of the two is small you are past 400. Since almost every real mediation has one weak path, that is the explanation for so many models with 120 participants finding nothing indirect. The step-by-step procedure is in sample size for mediation.

The five recurring mistakes. One, computing power after seeing the data and calling it a priori. Two, giving the effect size without saying where it came from. Three, planning for the main effect and testing the interaction. Four, forgetting attrition and finishing below the planned N without mentioning it. Five, naming the software without its version, which is precisely what stops anyone reproducing your number when they try.

Frequently asked questions

How do you report an a priori power analysis in APA 7?

With six pieces of information in the Method: the exact test you will run, α and whether it is one- or two-tailed, the target power, the effect size and its source, the resulting N (per group, with the actual power) and the software with its version and reference. The model sentence is “sample size was determined a priori using G*Power 3.1.9.7 (Faul et al., 2007); to detect a difference of d = 0.50 with a two-tailed t test, α = .05 and power .80, 128 participants are required, 64 per group (actual power = .80)”. Neither α nor power takes a leading zero; d does, because it can exceed 1.

What is post hoc power and why is it useless?

It is power computed after the analysis using the effect size you observed. It is useless because, with the same N and the same test, it is a decreasing function of the p value: it adds nothing to what p already tells you. In a two-tailed z test, p = .05 corresponds exactly to observed power of .50, so any non-significant result returns something below .50 as arithmetic, not as a diagnosis. Hoenig and Heisey (2001) named this the power approach paradox: the worse the p, the worse the observed power, always, which makes explaining a null result with it perfectly circular.

What alpha and what power should I use?

By convention α = .05 two-tailed and power .80, and both are conventions rather than rules. The .80 comes from Cohen (1988), who proposed it on the assumption that a Type I error is treated as about four times more serious than a Type II error. If your study is expensive, hard to replicate or feeding into a clinical decision, .90 or .95 defend themselves and only cost you sample. A one-tailed test lowers the N, but it is only defensible when the direction was preregistered; choosing it after seeing that two-tailed fell short is a different matter.

Where do I get the expected effect size if there are no previous studies?

In order of preference: the smallest effect you would call clinically meaningful (which does not depend on the literature, it depends on your field), the lower bound of the interval from a meta-analysis of the specific effect, and only then Cohen's (1988) benchmarks, labeled as an assumption. Your pilot is the worst source: with 20 people per group, a d of 0.40 carries an interval from −0.23 to 1.03, so planning on that point estimate is planning on noise. A single significant prior study will not do as it stands either: its effect is a ceiling, because being large is why it got published.

I already have the data and a reviewer wants power. What now?

A sensitivity analysis, which is the same calculation solving for the effect: you fix the N you have, α = .05 and power .80, and report the smallest detectable effect. With 96 participants, 48 per group, that is d = 0.58, and the sentence reads “a sensitivity analysis indicated that the study had .80 power to detect effects of d ≥ 0.58”. Pair it with the confidence interval around the observed effect and, if your hypothesis was one of absence, with an equivalence test. Then say out loud whether 0.58 is plausible in your area, because that is where the real limitation sits.

How do you cite G*Power in APA 7?

In text you name it with the exact version and the article reference, “G*Power 3.1.9.7 (Faul et al., 2007)”, and the reference list carries the article: Faul, F., Erdfelder, E., Lang, A.-G., & Buchner, A. (2007). G*Power 3: A flexible statistical power analysis program for the social, behavioral, and biomedical sciences. Behavior Research Methods, 39(2), 175–191. The version matters because formulae have changed across releases, and without it the calculation cannot be reproduced exactly. If you worked in R, cite the package (pwr, simr, WebPower) with the same level of detail.

With the exact test, α, the target power, the effect size and its source, the N and the software version, your a priori analysis is reported the way APA 7 asks; and if the sample was already closed, the sensitivity analysis says the only thing that can be said without misleading anyone. When the hard question is not the format but which minimum effect is defensible in your field, or whether the design can carry the hypothesis you want to test, that is what my statistical consulting is for.