Reviewer says my n is not independent

A reviewer saying your n is not independent claims your reported sample size counts measurements rather than independent units, so your test assumes an independence your data do not have. The objection arrives in many phrasings — “the authors treat each cell as an independent observation”, “what does n refer to here?”, “these are technical replicates” — and carries one meaning.

The objection is the most consequential statistical one you can receive, because unlike most it changes results by orders of magnitude rather than at the margin. It is also, usually, fixable without a single new experiment.

The comment is also common enough that experienced reviewers look for it by default. Lazic examined a single issue of Nature Neuroscience as a case study and found that 12% of the papers had pseudoreplication, with a further 36% suspected of it but impossible to judge because the reporting gave insufficient information (BMC Neuroscience 2010;11:5). Aarts and colleagues, reviewing 314 papers drawn from five neuroscience journals, found that a little over half involved nested data of some kind (Nature Neuroscience 2014;17:491–496). A referee raising the point is applying a standing expectation, not singling your manuscript out.

What the reviewer is claiming

Independence is a property of the experimental design, not of the measurements. The independent unit is whatever level the treatment was applied at and biological variation occurs at.

If you treated six mice and measured 25 cells from each, you have six independent units and 150 measurements. The 150 cells give you a more precise estimate of each mouse’s value — genuinely useful — but they do not tell you about mouse-to-mouse variation, which is the variation your comparison is against. A t-test on 150 cells uses a standard error computed as though you had 150 independent animals, and it will be far too small.

The same structure appears as: wells split from one culture, sections from one block, images from one slide, two tumours in one animal, repeated measures on one subject, and replicates pooled across experiments.

Two conditions decide the level, and both must hold. The treatment must have been applied to that level independently, and biological variation must occur between units of that level. A compound delivered in the drinking water of a cage of five mice was applied once, to the cage, so the cage is the unit. A compound given to a pregnant dam and assessed in her pups makes the litter the unit, not the pup. ARRIVE 2.0 turns this into a reporting requirement rather than a matter of taste: item 1b of the Essential 10 asks authors to state “The experimental unit (e.g. a single animal, litter, or cage of animals)”, and naming the unit once in the methods pre-empts most of what follows; see the ARRIVE guidelines.

The direction of the error is not always the same, and conflating the two is a common overcorrection. Treating clustered measurements as independent — the failure this page addresses — is anti-conservative: it makes p-values smaller than they should be. The mirror-image mistake, analysing genuinely paired or matched data (drug and vehicle dosed in the same animal, before-and-after in the same subject) with an unpaired test instead of the pairing, is usually conservative instead — it wastes power but does not manufacture a false positive. A reviewer writing “your n is not independent” is almost always pointing at the first kind. Do not assume every fix must widen your interval: for a genuinely paired design analysed correctly, using the pairing typically shrinks the interval, by removing between-subject noise, not by inflating n.

Common questions about pseudoreplication

What is pseudoreplication?

Pseudoreplication is treating non-independent measurements as separate independent observations. Measuring 50 cells from one animal produces 50 numbers, but the animal is the unit that received the treatment and varies biologically — so the true n is 1, not 50, because every cell shares that animal’s genetics, handling and environment.

What counts as my true n?

Your true n is the number of units the treatment was independently applied to and across which biological variation occurs — usually animals, donors, independently derived cell lines, or independent experiments run on separate days, never the measurements taken from each one. Counting cells, wells or sections as n is the error itself.

Is this the same as clustering in epidemiology?

Yes — clustering in epidemiology is structurally identical to pseudoreplication in bench science. Patients nested within clinics, students within schools and cells within animals all violate the same independence assumption, and the fix is the same family of methods: analysis at the cluster level, a random-effects model, or cluster-robust standard errors when clusters are numerous enough.

Decoding the phrasing you actually received

The wording of the comment tells you which level the reviewer suspects, and therefore which number in your manuscript to check first. Reviewers rarely write the word pseudoreplication; they write the specific version.

Each row points at a different fix, and answering the wrong one wastes a revision round. “Please clarify the experimental unit” can sometimes be answered with a sentence in the methods; “the authors treat each cell as an independent observation” never can.

Why it matters so much

The standard error shrinks with the square root of n. Going from a true n of 6 to a claimed n of 150 shrinks it fivefold, which moves p-values by orders of magnitude. A finding at p < 0.001 on the inflated n can be p > 0.2 at the correct one.

That asymmetry is why reviewers treat this comment as serious rather than pedantic, and why “we have added more cells” is the wrong response — it makes the reported n larger while leaving the real one unchanged.

The size of the error is governed by the intraclass correlation coefficient, ICC or rho, the share of total variance sitting between units rather than within them. Kish’s design effect converts it into a penalty: DEFF = 1 + (m − 1)rho, where m is the number of measurements per unit. At 25 cells per animal and an ICC of 0.5 — unremarkable for a phenotype that differs between animals — DEFF is 13, so 150 measurements carry the information of about 11 independent observations, not 150. ICC = 0 is the only value at which measurements are worth their face value, and it means the animals do not differ from one another at all.

Aarts and colleagues put a number on the consequence: in their simulations, ignoring the nesting drove the chance of declaring a null effect significant far above the nominal 5%, reaching the order of 80% in the most strongly clustered designs they modelled (Nature Neuroscience 2014;17:491–496). A test running at that false-positive rate is not a weakened test; it is a coin weighted to say yes. Eisner reached the same conclusion for cellular physiology and titled the paper accordingly — “Pseudoreplication in physiology: More means less” (Journal of General Physiology 2021;153:e202012826).

Epidemiologists have a name and a standard fix for the same arithmetic. Pooling a cluster-randomised trial into a meta-analysis alongside individually randomised trials requires dividing its effective sample size by the same design effect, 1 + (m − 1)rho, before the two are combined. The correction does not care whether the clusters are hospital wards, classrooms, or wells on one plate — only that measurements inside a cluster share a source of variation that measurements between clusters do not.

Establishing whether the reviewer is right

Settle the question before you draft a response, using three numbers your manuscript already reports in three different places. No statistical test identifies pseudoreplication.

Compare the legend n with the animal count in the methods. A legend reading n = 120 in a study whose methods describe eight mice is the whole finding. Where the legend gives no n at all, the reviewer is entitled to assume the worst.

Read the degrees of freedom. A two-sample t-test on six animals, three per group, has 4 degrees of freedom; reported as t(148) it was run on 150 measurements. Degrees of freedom are the most reliable tell because they are printed in the result and cannot be reconciled with a small animal count by any reading.

Apply the one-question test. Could you increase your n tomorrow without running a new experiment? If going back to the microscope and counting more cells raises your n, then your n counts measurements and it is not a sample size. This takes ten seconds and needs no statistical knowledge — it is the same test set out on what is pseudoreplication.

Check the p-value’s behaviour. If your p-value improved every time you measured more cells from the same samples, the standard error was being computed at the wrong level; that symptom has its own page, my p-value gets smaller with more cells.

Journals increasingly settle the definitional part for you. The design and analysis guidance the British Journal of Pharmacology directs its authors, reviewers and editors to defines group size as the number of independent values, not the number of measurements taken, so a single sample assayed five times counts once (Curtis et al., British Journal of Pharmacology 2018;175:987–993). At a journal with such a policy the comment is a compliance check rather than a referee’s opinion, and an editor can act on it without a statistical reviewer.

Questions about checking your own data

Do technical replicates count as n in a t-test?

No. Technical replicates measure the same biological sample repeatedly to estimate measurement error, not to estimate biological variation, so they cannot substitute for independent units in a t-test’s degrees of freedom. Average the technical replicates into one value per biological unit first, then run the test on the number of biological units, not the number of measurements.

Can I just write “n = number of cells” in my methods and move on?

You can write it, but a reviewer applying ARRIVE 2.0 or a journal’s group-size policy will still ask what independent unit the cells came from. Naming cells as n is only defensible when the research question is genuinely about variation within one animal or culture, not a between-group comparison — state which question you are asking, explicitly, in that same sentence.

Why did my p-value get smaller every time I added more cells?

Because your standard error was being computed as though each new cell were a new independent observation, when it was really adding precision to an estimate for the same one or two animals. That symptom — p shrinking with every added measurement rather than every added animal — is the single most reliable diagnostic for pseudoreplication; see my p-value gets smaller with more cells.

The remedies, in order of preference

Pseudoreplication has four standard remedies and one prohibition, and the first remedy is correct in the great majority of designs. Choose by design structure rather than by which one preserves the p-value.

Summarise to the independent unit. Take the mean of your 25 cells per mouse, then run the comparison on six values. Simple, transparent, and immediately understood by any reviewer. You lose the visual richness of a 150-point plot, but you can still show the cells with the per-animal means overlaid — many journals now prefer this figure. Use the median rather than the mean where the within-unit distribution is skewed or holds a few extreme cells, and say which you used.

Fit a mixed-effects model with a random effect for animal, culture, or experiment. This uses all the data while estimating variance at the right level, and it is the better answer when your groups are unbalanced or you have several nesting levels. Say which package and which random effect structure you used. In R that means naming lme4 with lmerTest, or nlme, giving the formula in full, and stating whether denominator degrees of freedom came from the Satterthwaite or the Kenward–Roger approximation; Kenward–Roger is the more conservative and is the usual choice when units are few. In SAS the equivalent is PROC MIXED with DDFM=KR, in Stata mixed. “A mixed model was used” is not reproducible, and reviewers say so on the second round.

For paired structures, use the pairing: two tumours per animal call for a paired analysis or an animal random effect, not an unpaired test on twelve tumours.

Use cluster-robust standard errors or generalized estimating equations where the target is the population-average effect and the variance structure is not itself of interest. GEE with an exchangeable working correlation and the animal as the cluster gives a valid marginal estimate, but its sandwich standard errors are unreliable when clusters are few — under roughly 30 to 40 clusters, prefer a mixed model or summarising. Note also that GEE’s marginal (population-average) effect and a mixed model’s conditional (subject-specific) effect are the same quantity for a linear model but not for a logistic or Poisson outcome — the two can differ in magnitude even when both are estimated correctly, so state in the methods which one you are reporting.

Do not pool across independent experiments and test on the combined observations. Between-experiment variation is usually the largest source of variability, and pooling hides it entirely. It is also the form most likely to be a disguised batch effect, because the day of an experiment carries reagent lot, passage number and operator with it.

Questions about fixing the analysis

Does a mixed-effects model let me keep my large n?

A mixed model lets you use all the data, which is not the same as keeping the p-value. The model estimates variance at the correct level, so the inference reflects your true number of independent units. The interval usually widens; that is the point, and a model that does not widen it is worth checking for a singular fit.

Can I count cells as n if they come from different dishes?

Only if the dishes are genuinely independent — separately derived cultures, not aliquots split from one flask or suspension. Wells split from a common source share whatever happened to that source, including its exact passage number and media batch, so they are technical replicates and count once, however many wells were plated from it.

How many biological replicates do I actually need for RNA-seq?

There is no fixed number that fits every design, but three independent biological replicates per condition is the practical floor most RNA-seq pipelines assume, because tools such as DESeq2 and edgeR need at least that many per group to estimate within-group dispersion at all. Three replicates only detects large, consistent effects; more replicates buy statistical power, not more cells per replicate.

When the obvious remedy is unavailable

Summarising to the unit fails in a small number of recognisable situations, and each has an accepted alternative that a reviewer will accept if you name it.

Too few units to fit a random effect. Three independent experiments will not support a well-identified variance component, and lme4 frequently returns a singular fit with the between-unit variance estimated at exactly zero. Report the singular fit rather than quietly deleting the random effect, and fall back to the summarised analysis on three values, stating the model that failed and why. With only three to five aggregated values per group, also reconsider the test itself: a Welch’s t-test still assumes the per-unit means are approximately normal, and a permutation test or Wilcoxon rank-sum test avoids that assumption when you are not willing to make it at such a small n.

The outcome is a proportion or a count. Averaging binary cell-level calls per animal and testing the proportions is transparent and usually acceptable; a generalized linear mixed model with a binomial or negative binomial family is the alternative when the per-animal denominators differ widely.

The question is genuinely at the measurement level. A study of how a property is distributed across cells within one individual is a within-unit question, and the cells are the right unit for it. What that design cannot support is a between-group claim, so keep the two analyses and their two claims visibly separate in the text.

Only one independent unit exists. A single patient-derived line, a single donor, a single field site. No analysis rescues an n of 1, and the honest presentation is descriptive, with the limitation written as a specification of what the experiment establishes rather than an apology — see how to write a limitations section.

The grouping was never recorded. Where experiment of origin was not tracked, the nesting cannot be reconstructed after the fact. Say so, analyse at the level you can defend, and record the grouping variable next time; it is one column.

Responding when the reanalysis changes your result

Reanalysis at the correct unit sometimes removes the result. This is the hard case and it is worth being straight about.

If the effect survives at the correct unit with a wider interval, report it and say so. If it does not survive, you have three honest options: report it as non-significant with the effect size and interval, reframe the finding as preliminary and say what would test it properly, or collect more independent units. What you cannot do is keep the original analysis.

Reviewers who raise this comment are watching for exactly that. A revision that adds a mixed model in the supplement while the abstract keeps the original p-value gets rejected, and deservedly.

If you choose the third option, do the arithmetic first. Because the design effect scales with the number of units and not with the number of measurements, six more animals at 10 cells each buys more information than 500 more cells from the animals you already have. Aarts and colleagues reach the same conclusion from the power side: optimising a nested design nearly always means collecting more truly independent observations rather than more observations per object. Any statistical power calculation built on the measurement count is void for the same reason, which is why a sample size justified after the fact from the number of cells measured persuades nobody — see post-hoc power.

What to write in the response letter

Answer this objection in three moves and nothing else: name the experimental unit, re-run the analysis at that level, and update every number that changed. A worked shape, for a study of six animals per group with 25 cells each:

We agree. The experimental unit is the animal, and the original analysis treated the 150 cells per group as independent observations. We have re-analysed by taking the per-animal mean of the 25 cells and comparing the six values per group (Welch’s t-test, t(9.4) = 2.41, p = 0.038); the mixed-effects model with a random intercept for animal, fitted in lme4 with Kenward–Roger degrees of freedom, gives the same conclusion and is now reported in Supplementary Table 3. The difference is 18% (95% CI 1.2% to 34%) rather than the 19% previously reported, and the p-value moves from p < 0.001 to p = 0.038. Figure 2b now plots cells in grey with per-animal means overlaid, and all figure legends state that n is animals. The abstract, Results and Methods have been updated accordingly.

Four features make that paragraph work, and each is checkable by a reviewer in one pass. It concedes rather than argues. It names the unit as a fact about the design. It gives the number that changed and the number that did not. And it lists every location in the manuscript that was touched, so the reviewer does not have to hunt for an unrevised copy of the old p-value. See how to write a response to reviewers for the letter structure around it, and a worked response letter for the surrounding format.

Two things not to do. Do not argue that the effect is obvious from the cell-level data — the reviewer is not disputing that the cells look different. And do not present both analyses and invite the reader to choose; a manuscript reporting two incompatible p-values for one comparison has made the reviewer’s point for them.

What changes besides the analysis

Correcting the unit changes at least five places in a manuscript, and reviewers check all of them on the second round.

Every figure legend. State the number of independent units and what they are, and separately the number of measurements: “n = 6 animals per group; 25 cells measured per animal; statistics computed on per-animal means.” Add the test and the degrees of freedom so the level of inference is checkable without reading the methods.

Every figure. Plot the measurements lightly and overlay the per-unit means as larger points, colour-coded by independent experiment. Lord, Velle, Mullins and Fritz-Laylin published this design as the SuperPlot (Journal of Cell Biology 2020;219:e202001064). A SuperPlot drawn correctly but still analysed at the cell level is still pseudoreplicated, so state in the legend which level the error bars and the p-value came from. Where the measurements are image-derived, the legend also has to say how many fields per section and how many sections per animal contributed, because that is the next thing a reviewer asks for.

The abstract. Any effect size, interval or p-value quoted there must be the corrected one. This is the single most common place the old number survives.

The methods. One sentence naming the experimental unit, one naming the model and its random effect structure, one naming the software and version.

The sample size statement. Six animals is a defensible n; it is also small, and correcting the unit often converts a statistics objection into a sample size objection. Anticipate that in the same revision rather than discovering it in round three.

When the objection overreaches

Reviewers occasionally push this comment past what it supports, and three specific pushbacks are legitimate if stated without heat.

Taking many measurements is not the error. Running a sample in triplicate detects pipetting error and instrument drift, and measuring 200 cells per animal rather than 5 gives a better estimate of each animal’s value. The Curtis guidance requires one consensus value per unit to go forward into the analysis; it does not discourage technical replication.

Nested designs are not the error either. Nesting is how biology works, and a correctly analysed nested experiment is stronger than a flat one because it separates the variance you care about from the variance you do not.

And the objection does not reach the separate question of whether an experiment was repeated. Independent replication and independent units are different requirements, and a paper can satisfy one and fail the other — see reviewer says the experiment was not replicated. A third and distinct objection is that the test itself was the wrong one for correctly counted units, covered at reviewer says I used the wrong statistical test.

Where a reviewer is wrong on the facts — the cultures were independently derived, the model already carried a random effect they missed — say so once, point to the line, and offer the clarifying sentence you have added. Do not spend a paragraph on it.

Frequently asked questions

How do I respond when a reviewer says my n is not independent?

The right response to “your n is not independent” concedes the point, names the experimental unit, re-runs the analysis at that level, and updates the abstract, results, figures, legends and supplement together — not just one of them. State both the number that changed and the number that did not, and list every location you revised.

The reviewer says these are technical replicates — can I argue back?

Only on the facts. If the cultures were independently derived, or the model already carried a random effect the reviewer missed, say so once and point to the line. Arguing that the cell-level difference is visually obvious concedes the statistical point while appearing to dispute it.

Reviewer 2 says my n is not independent, what do I do?

Read past the shorthand: “Reviewer 2” phrasing usually still means one specific claim — that your reported sample size counts measurements, not independent units. Find the number in question in your legends and methods, identify the true experimental unit, and follow the same three moves as any version of this comment: concede, rename the unit, and re-run the analysis at that level before you draft a single word of rebuttal.

Catching it before submission

Pseudoreplication is the objection the pseudoreplication agent exists for. It reads every figure legend, determines what each n counts, reconstructs the physical structure of the experiment from the methods, and reports every place the stated n exceeds the number of independent units. It is worth a slot on any manuscript where measurements come from a hierarchy — which is nearly all in vivo and cell biology work.

PerfectPaper reconciles the n in each figure legend against the animal, donor and culture counts in the methods, and reports each place the reported sample size counts measurements rather than independent units. The same reconciliation catches the sequencing and cytometry version, where thousands of single cells from one donor become thousands of rows in a differential test and pseudobulk aggregation to the donor is the standard fix.

Related objections: sample size is too small, and the full family on responding to statistical reviewer comments.

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