The n = 30 rule: where it came from and why it is wrong

Someone told you with complete confidence: thirty is fine. Maybe your supervisor, maybe the methods chapter you downloaded, maybe the friend who submitted last year. Now you have 34 participants, a result that refuses to come out, and the uncomfortable suspicion that the number your entire study was built on was never really chosen by anyone. The question keeps resurfacing on r/AskStatistics — the most upvoted thread on it carries 83 votes and 138 comments — and always for the same reason: 30 gets taught as if it were a threshold, and it is not one. It is a historical leftover. Here is where it came from, what the theorem people cite actually says, and what sets the number you need.

Where the 30 actually came from

The first source is a table. Through the seventy-odd years when a test was settled by turning to the back of the book, t tables listed degrees of freedom one by one up to 30 and then jumped to 40, 60, 120 and ∞. The reason is arithmetic: the two-tailed critical value at α = .05 is 2.042 at 30 df, 1.980 at 120 and 1.960 in the normal limit. Past 30, the small-sample correction stops showing up in the second decimal and there is no point printing more rows. That is where «over 30 is a large sample» came from, and it was true about the table and about nothing else.

The second source is the central limit theorem chapter of every introductory textbook, home of the sentence «for n ≥ 30 the sampling distribution of the mean is approximately normal». The 30 turns up there with no proof and no conditions, because it is a rule of thumb: it behaves reasonably for mildly skewed variables and it fails for the rest. No version of the theorem mentions 30, and no version could.

Both shortcuts are harmless while they stay in the classroom. The trouble starts when the number gets copied into a methods section as if it were a criterion, and then someone — a reviewer, an ethics committee, an examiner — asks the one question that matters: how did you determine your sample size? If the honest answer is «I was told 30 was enough», the study has no sample size justification, whatever the number of participants turns out to be.

The central limit theorem, told properly

Here is what the theorem says: if you draw independent observations from a population with finite variance, the distribution of the sample mean approaches a normal distribution as n grows. Three things get lost in the pocket version. First, it is about the mean, not about your data. Your variable stays exactly as skewed with 30 people as with 3,000; what becomes normal is the behavior of the average if you were to repeat the study endlessly. Second, it is an asymptotic statement about a limit, so it cannot certify any particular n. Third, it demands independence. If you measure 30 pupils from the same classroom, or 30 patients spread across four therapists, the theorem is telling you nothing about the thing you care about.

The speed of convergence, on the other hand, can be bounded, and it depends on skewness: the approximation error falls as 1/√n and rises with the third moment of the variable (the Berry-Esseen bound). Cochran (1977) turned that into a usable rule: for a test on the mean to behave, you want n > 25 × skewness². For a skewness of 1, 25 cases. For a skewness of 2 — symptom counts, reaction times, drinking days in the past month — 100. For a skewness of 4, standard territory for low-frequency behaviors, 400. The 30 appears nowhere, and what decides is the shape of your variable rather than a round number.

There is also a long list of quantities you estimate every week that the theorem does not cover at all: a correlation, the ab product of a mediation (skewed by construction, which is exactly why we bootstrap it), a between-group variance, a fit index, a median, an odds ratio. No sample mean is being normalized there. Even in the case it does cover, one subtlety survives: with skewed data the sample mean and the sample standard deviation stop being independent, and since the t statistic divides one by the other, the real Type I error drifts away from the nominal one, particularly in one-tailed tests.

And no, a non-significant Shapiro-Wilk at n = 30 fixes none of the above: at that sample size the test has almost no power to reject, so a high p there means «I could not see the skew», not «there is none». The full argument is in why the Shapiro-Wilk normality test gets read backwards.

Even with a perfect approximation, you would still see nothing

Suppose now that the approximation is flawless and your variable is symmetric. You still have a bigger problem, and it is the one that actually sinks studies of 30: at that sample size almost nothing is visible. With 30 per group, α = .05 two-tailed and .80 power, the smallest effect you can detect is d = 0.74. That is a chasm between groups, well above what meta-analyses estimate for psychological interventions against an active control.

If the real effect is d = 0.50 — Cohen's «medium» (1988) — then 30 per group gives you .48 power: a coin flip. If it is d = 0.40, power drops to .33, and reaching .80 would take 100 per group. And if your 30 is the total, meaning 15 per group, the minimum detectable effect climbs to d = 1.06 and power for a d = 0.50 sits at .26.

With correlations the sum is even easier to check, because there is a fixed cut-off: at N = 30, any r below .361 comes out non-significant, no matter what. The typical effect in social psychology is around r = .21 (Richard, Bond and Stokes-Zoota, 2003, across a century of literature). At N = 30, that effect gives t(28) = 1.14, p = .265, and power of 20%: four times out of five, when the relationship is genuinely there, your study will conclude there is nothing. Seeing it at .80 power takes N = 176; an r = .30 takes N = 85.

That is the real price of the myth. It is not that the analysis «cannot be run»: it runs, a number comes out, and that number almost always says «non-significant» even when the phenomenon is real. What follows is a manuscript that reads a lack of precision as an absence of effect (what to do when nothing is significant) and an effect size whose interval is so wide it is compatible with almost anything (how to interpret Cohen's d).

The four things that do set the number

Sample size is not a property of your field or of the kind of project you are doing: it is the solution to an equation. Four things go in and the number comes out; and if the N is fixed for you by circumstance, the equation still holds — what you solve for is the smallest effect you could have seen. First input: the smallest effect you want to be able to detect. Not the one you expect, and not the one from the previous study: published effects are inflated by selection, so designing against them leaves you short every time. It is the smallest effect that would change something — the difference that justifies changing a protocol, the one a patient notices, the one that makes two theories predict differently. Lakens (2022) gave the practice a name, sample size justification, and set out the full menu of defensible ways to pin that number down.

Power. The conventional .80 (Cohen, 1988) means you accept missing the effect one time in five when it is really there. For confirmatory work, or for a study you will never be able to repeat, .90 or .95 is the sensible choice, and it costs people: with a d = 0.50 you go from 64 participants per arm to 86 at .90 power and 105 at .95.

Alpha, and how many tests you plan to run. If the protocol lists twelve outcomes and you intend to correct for them, the effective alpha per test falls and the required N rises. Deciding that after seeing the data is a different and worse problem.

The design. It carries more weight than the other three and gets the least attention, so it gets its own section.

For the most common test — two independent groups, α = .05 two-tailed, .80 power — the reference numbers are these: 394 per group for a d = 0.20, 64 for a d = 0.50 and 26 for a d = 0.80. Look at the last one. Twenty-six. That is the myth's real family resemblance: 30 per group is roughly the sample you need when the effect is large in Cohen's sense, so adopting it as a general rule means quietly assuming that yours is. For your own parameters, the sample size calculator does the arithmetic, and the step-by-step procedure is in how to calculate the sample size for a thesis.

Design moves the number more than anything else

Take the same 60 people. Split into two independent groups, a d = 0.50 gives you .48 power. Measure 30 people twice instead, before and after, with a correlation of .60 between the two measurements: the effect in the metric of the test becomes d_z = 0.56 and power rises to .84 with half the participants. You have not changed the phenomenon or the instrument. You have changed where the error piles up.

Design can also work against you invisibly. If your 30 patients sit in therapy groups of 10 and the ICC is .10, the design effect is 1 + (10 − 1) × .10 = 1.9, and your effective sample is 16 people rather than 30. The same goes for pupils within classrooms, patients within therapists and sites within a multicentre trial. If the dependency is there and the analysis ignores it, the standard error comes out too small and the p value too pretty.

Reliability is paid for in participants too. A true correlation of .30 measured with two instruments at Cronbach's α = .70 shows up attenuated to .21 in your data: you have turned an effect that needed 85 people into one that needs 176, purely by measuring with mediocre scales. Predictors cost the same way. With N = 30 and five predictors, an R² = .20 sounds respectable until you correct for degrees of freedom: adjusted R² = .033, F(5, 24) = 1.20, p = .339. The model explains nothing; the .20 was overfitting capacity.

Interactions are the extreme case. The contrast for an interaction carries twice the standard error of a main effect contrast, so detecting an interaction half the size of the main effect takes sixteen times the sample. A 2×2 with 30 per cell — 120 people, which sounds generous — is almost never able to see the interaction it was designed around. One last thing: your N is whatever survives. If the calculation asks for 64 per arm and you expect 15% attrition, you recruit 76.

When 30 (or fewer) is genuinely defensible

There are places where 30 holds up perfectly well, and they are worth knowing, because they are precisely the ones where nobody is claiming to test a hypothesis. The first is the pilot study: the goal is not to estimate the effect, it is to find out whether the protocol works, how many people drop out and how variable your measure is. Numbered recommendations do exist there: 12 per group (Julious, 2005), or 30 per group when the aim is to estimate the standard deviation you will use to power the real study (Lancaster, Dodd and Williamson, 2004). It is one of the very few real references where a 30 shows up, and it is for a design that tests nothing.

The second is designs with many observations per person. Thirty participants with 60 trials each, or with 40 experience-sampling prompts, carry an enormous amount of information about level 1 effects, the ones that happen within a person. The catch is that the same study is desperately poor at level 2: differences between people, trait moderators, cross-level interactions. Maas and Hox (2005) showed that standard errors at the upper level need something like 50 units before they stop being biased. With 30 people you can say a great deal about within-person dynamics and almost nothing about who it works for.

The third is the family of designs that does not reason through power at all: single-case designs with a baseline and repeated measurement, qualitative work with a saturation criterion, content validity work with expert judges. And here is the rule that unifies all three: 30 is defensible when you can say what those 30 are for. It stops being defensible at the exact moment you use them to run a confirmatory test and draw a conclusion about a population.

How to justify your number in the methods (and what to do if the data are already in)

The justification fits in three sentences and always carries the same parts: the smallest effect of interest and where it comes from, the parameters of the calculation, and the allowance for attrition. It reads like this: «The smallest effect of interest was set at d = 0.50 between arms, half a standard deviation on the outcome measure and the change this clinical literature links to patient-reported improvement. With α = .05 two-tailed, power of .80 and an independent-samples t test, the calculation requires 64 participants per arm; allowing for 15% attrition, 76 per arm were recruited (G*Power 3.1.9.7).» Everything is there: the figure, its origin, and how to reproduce it.

If the data are already collected and the number was handed to you by circumstance — a small clinical sample, a single cohort, the length of the funding — there is still an honest way out, and it is not post hoc power computed from the observed effect, which is a transformation of the p value and adds no information. It is the sensitivity analysis: with this N, this alpha and .80 power, what is the smallest effect I could have detected? With 34 participants across two groups, the answer is d = 0.99. That sentence goes straight into the limitations and makes clear what the study cannot conclude. The distinction between the two, in seventh-edition format, is in how to report a power analysis in APA 7.

In the discussion, watch your wording. A study of 30 people with a non-significant result has not found that there is no effect: it has estimated the effect very imprecisely. Report the effect size with its confidence interval, say what that interval rules out and what it does not, and do not turn a shortage of power into a finding.

Frequently asked questions

Is 30 participants enough to run a t-test?

The t test does not ask for 30: it asks for independent observations and a roughly normal sampling distribution of the mean. With a symmetric variable, 15 is plenty; with a skewness of 2 — counts, reaction times — you need around 100 under Cochran's rule (n > 25 × skewness²). And «being able to run the test» is not the same as «the test being able to see anything»: with 30 per group you only detect effects of d = 0.74 and above.

Is it 30 per group or 30 in total?

Neither one is a criterion, but the gap between them is huge. With 30 per group (60 people) the minimum detectable effect at .80 power is d = 0.74. With 30 in total (15 per group) it climbs to d = 1.06, and power for a medium effect of d = 0.50 sits at .26. Whoever says «30 is enough» has usually not specified which of the two, and that is the first sign the number did not come out of a calculation.

How many participants do I need for my dissertation?

It depends on the smallest effect you want to detect, the design and the power, not on the type of project. To compare two groups at α = .05 with .80 power: 26 per group if the effect is large (d = 0.80), 64 if it is medium (d = 0.50), and 394 if it is small (d = 0.20). For a correlation: 85 if you expect r = .30, and 176 if you expect r = .21, which is the typical size in social psychology. A within-subject design or any clustering shifts these numbers a long way, so run the calculation on your design rather than on a textbook's.

I already have 34 participants and nothing is significant. Should I run post hoc power?

Not if by post hoc you mean computing power from the effect you observed: that is a function of the p value and will always tell you power was low whenever the result is non-significant. What does work is a sensitivity analysis: with 34 people across two groups, α = .05 and .80 power, the minimum detectable effect is d = 0.99. That sentence belongs in the limitations, and it explains the result without inventing anything.

My data are not normal. Does the central limit theorem save me?

For the mean, and only if your n is big enough given the skewness of the variable (a skewness of 2 takes around 100 cases). It does not save you for a correlation, for the indirect effect of a mediation, for a variance component or for a fit index, because there is no sample mean being normalized there. And it adds no power whatsoever. If the variable is a count, modeling it as one (Poisson, negative binomial) almost always beats hoping that 30 cases will fix its shape.

My supervisor says 30 is fine. How do I push back?

Do not argue about the number, bring the calculation: «with 30 per group we can only detect effects of d = 0.74 or larger; the effect this intervention literature reports is d = 0.40, which would take 100 per group. With the sample we can realistically get, there are three ways out: switch to a within-subject design, call the study a pilot, or cut the number of tests.» That is a design conversation and it can be had; «30 feels low to me» is an opinion and goes nowhere.

Keep this much: 30 is not a threshold, it is the residue of a printed table and of a rule of thumb told badly. The number you need comes out of four decisions — the smallest effect you want to be able to see, power, alpha and the design — and skipping any of them costs the study its meaning before it starts. If the data are already collected, do not paper over it with post hoc power: state the effect you could have detected, report the one you got with its interval, and let the reader see how much precision you actually have.