Four Identical Standard Errors: Defending a Mixed Model in Front of Your Professor

Abstract

A mixed model with a repeated factor prints the same standard error at every level, and somebody asks whether the software is broken. It is not. Under a balanced design with one pooled residual variance, the standard error of every unit-specific contrast is the square root of twice the total variance over n, an expression with no unit index, so identical values are what the algebra requires. This closing post derives that statement, names the four ingredients it depends on, then breaks them on purpose: with twelve missing measurements at one site, that contrast's standard error moves from 0.71 to about 0.74. It also refuses the opposite error, since legitimate output never validates its own assumption. Readers leave with a four-step spoken defence and a reporting checklist.

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One Number Per Person: Linear Mixed Models from the Ground Up · Post 8 of 8 — the series finale.

Where we are. This series is about studies in which one participant contributes several rows of data — here, four skin sites measured in each of 80 people — so the rows cannot be treated as independent. The repair used throughout is a mixed model, which gives every participant one personal offset, $b_i$, added unchanged to each of that person's rows; this single number is what makes a person's own measurements travel together. Seven posts have followed it into a covariance matrix, into an intraclass correlation, into the general equation $V_i = Z_i G Z_i' + R_i$, and into the two places where any mixed model can be enriched. The previous post, Population-Averaged Alternatives: GLS, GEE, and Where the Linear Model's Luck Runs Out, showed what happens when a model declines to explain where the correlation came from and simply states what it is. This closing post converts the whole series into one paragraph you can defend out loud, in front of somebody who is not yet convinced — and it starts, as these things usually do, with a raised eyebrow.

You do not need Posts 1 to 7 to read this one; everything it uses is re-introduced below. If you would rather start from the gentler overview, the map of the whole series is here: series guide.

Every number in this series comes from simulated teaching data; later posts introduce clearly labelled variant simulations. It is not an empirical finding, it describes no real cohort, and it must not be cited as evidence about skin physiology.

The scene

The output is on the screen. The model is the one this series has been fitting since Post 1: transepidermal water loss (TEWL, g·m⁻²·h⁻¹) measured at four standardised non-lesional skin sites in 80 simulated adults, 40 with moderate atopic dermatitis and 40 without atopic disease, with a site × group interaction, three person-level covariates, and one random intercept per participant. Four sites, four estimated AD − control differences, and a standard-error column that reads the same number four times.

site	AD − control (g·m⁻²·h⁻¹)	SE (g·m⁻²·h⁻¹)
forearm	6.0	0.71
hand	8.0	0.71
shin	3.0	0.71
back	5.0	0.71

The point estimates are not equal — the simulation was built with a real site × group interaction, and the four differences of 6.0, 8.0, 3.0 and 5.0 reflect it. Only the uncertainty column repeats. The question that follows is almost always the same, and it is a fair one: did the software copy a number down the column?

The short answer, before any algebra

It did not. Nothing in the estimation has gone wrong, and the equality is not a rounding artefact that would dissolve at more decimal places. Before any formula appears, here is why in the language of the clinic.

Start with the reason the column looks wrong. In almost every table a clinician reads, each row carries its own standard error, because each row rests on a different number of patients and a different amount of scatter: the estimate from a subgroup of 30 is less precise than the estimate from a subgroup of 300. Four identical values in the uncertainty column therefore look like a copy-and-paste accident.

They are not, because this design hands every site exactly the same amount of information. All four sites were measured in the same 80 participants — the same 40 with atopic dermatitis and the same 40 without, at every site, with nobody missing — and the model was asked to describe all four sites with one shared noise level rather than four separate ones. The same people, the same number in each group, and one shared variance: whatever precision is available at the forearm is, by construction, the precision available at the shin.

A ward analogy makes it concrete. Suppose the same 80 patients have their weight recorded at four different clinics, on scales you have decided to treat as equally precise. The four mean weights may well differ, and that difference is a finding. But how precisely you know each clinic's mean is identical across the four, because the same people were weighed the same number of times on instruments you assumed to be equally good. The means are allowed to differ; the uncertainty about them is not.

This is also why the repetition survives a change of software. Fit the same model with the same assumptions in R or in Stata and the same repeated column comes back, because both programs are evaluating an expression in which nothing site-specific appears at all — only a between-person variance, a residual variance, and a number of participants. The repetition is arithmetic rather than a display bug, and it holds to as many decimal places as you care to print.

One warning belongs here, and the rest of this post collects it in full: the equality tells you what you assumed, not whether you were entitled to assume it. A model instructed to use one shared noise level will report equal standard errors even when the sites are genuinely not equally noisy. That is the second half of the defence, and it is the half that matters more.

To see the machinery behind all of this, three quantities that are routinely spoken of as if they were one must first be separated.

Three quantities that are routinely confused

Before the hard part: The three quantities below stay straight if each is attached to one clinical question. How different are patients from one another? That is the raw SD. How far does one reading sit from that patient's own usual level? That is the residual SD. How sure am I about the average I have just estimated? That is the standard error. Only the third one shrinks as you recruit more people, which is exactly why it can be identical at four sites whose raw spread is not.

The word "variability" is doing at least three jobs in any mixed-model output, and a defence that confuses them will collapse under the first follow-up question.

First, the raw standard deviation at a site describes how far individual measurements at that site scatter around the site mean, across all participants in a group. In the simulated dataset the model-implied version of that spread, holding the person-level covariates fixed, is the marginal SD $\sqrt{\tau^2 + \sigma^2} = \sqrt{10.00} \approx 3.16$ g·m⁻²·h⁻¹ — and note that it contains the between-person spread, because two participants measured at the same site genuinely differ. An SD computed directly from the raw column would be at least this large, since it also carries whatever variation age, sex and phototype explain.

Second, the residual standard deviation describes what is left after the mean structure and the person effect have been removed: how far one site sits from that participant's own profile. Here it is $\sqrt{\sigma^2} = \sqrt{3.75} \approx 1.94$ g·m⁻²·h⁻¹, and the between-person SD it excludes is $\sqrt{\tau^2} = 2.50$.

Third, the standard error of an estimated site mean describes how precisely the population mean at that site has been located, given the sample size. It is 0.50 g·m⁻²·h⁻¹ in this design. It is not a description of the data at all; it is a description of the estimate.

The non-implication should be stated flatly, because it is the load-bearing step of the whole defence: $\text{SD}_{\text{shin}} \neq \text{SD}_{\text{forearm}}$ does not imply $\operatorname{SE}(\widehat{\mu}_{\text{shin}}) \neq \operatorname{SE}(\widehat{\mu}_{\text{forearm}})$. The two statements are about different objects, and one does not travel to the other without an assumption you are free to inspect.

The formula with no site index in it

Before the hard part: The next formula is short, and its punchline is visual rather than algebraic. Look at the right-hand side and try to find anything in it that says forearm, or hand, or shin. There is a between-person variance, a residual variance, and a number of participants — and no site anywhere. A quantity whose formula never mentions the site cannot take a different value at a different site.

Under the simulated Spec A structure — one random intercept, one pooled residual variance, four sites measured in every participant, 40 participants per group — the standard error of an estimated site mean within one group has a closed form:

\[ \operatorname{SE}(\widehat{\mu}_{j}) \;\approx\; \sqrt{\frac{\tau^2+\sigma^2}{n}} \;=\; \sqrt{\frac{6.25+3.75}{40}} \;=\; \sqrt{\frac{10.00}{40}} \;=\; \sqrt{0.25} \;=\; 0.50 \]

Read the right-hand side and look for the site. It is not there. The expression contains a between-person variance, a residual variance and a sample size, and the site index $j$ appears nowhere at all. The AD − control contrast at a site compares two independent groups of 40, so its variance is the sum of two such quantities:

\[ \operatorname{SE}(\widehat{\Delta}_{j}) \;\approx\; \sqrt{\frac{2(\tau^2+\sigma^2)}{n}} \;=\; \sqrt{\frac{2\times 10.00}{40}} \;=\; \sqrt{0.50} \;=\; 0.71 \]

Again there is no $j$ on the right. The four numbers in the output column are equal because the quantity they estimate is, under these assumptions, literally the same quantity computed four times. Equality here is not a coincidence to be explained away; it is what the expression says.

Two claims are being made in that paragraph, however, and it is worth separating them before somebody separates them for you. The first is the equality of the four standard errors, and it is exact. It follows from the symmetry of the design matrix, as the next section shows, and it survives the addition of person-level covariates untouched. The second is the common value of 0.71, and it is only a plug-in magnitude, computed from the generating variance components in an unadjusted cell-means model. A fitted model — with $\tau^2$ and $\sigma^2$ estimated from the data and with age, sex and phototype in the mean structure — will therefore print four numbers that are still identical to one another but sit a little away from 0.71. The within-person figure of 0.43, derived further down, is the one exception: person-constant covariates cancel in a within-person difference, so adjustment cannot move it at all.

The general version: contrast geometry

Before the hard part: This section restates the same argument in the language a methodologist will ask for, and it can be skipped without losing the thread. The idea underneath the matrices is simple. All four site comparisons come out of one fitted model and one shared table of uncertainties; the four comparisons merely pick different entries out of that table. When the design is balanced, the entries they pick sit in mirror-image positions, so the four calculations return the same number.

The closed forms above are the arithmetic special case. The general statement — the one to give a methodologist — is about the geometry of contrasts. Any linear contrast $\widehat{\Delta}_{s} = c_s'\widehat{\beta}$ has

\[ \operatorname{SE}(\widehat{\Delta}_{s}) \;=\; \sqrt{c_s'\,\operatorname{Var}(\widehat{\beta})\,c_s}, \qquad \operatorname{Var}(\widehat{\beta}) = \left(\textstyle\sum_i X_i' V_i^{-1} X_i\right)^{-1} \]

The four site-specific AD − control contrasts share one fitted model and one $\operatorname{Var}(\widehat{\beta})$; the vectors $c_{\text{forearm}}, c_{\text{hand}}, c_{\text{shin}}, c_{\text{back}}$ differ only in which indicator and interaction columns they select. When every participant contributes exactly one observation at every site, when the two groups are of equal size, and when $V_i$ is the same compound-symmetric matrix for everyone, those selected positions occupy structurally symmetric places in $\operatorname{Var}(\widehat{\beta})$. The four quadratic forms are therefore equal:

\[ c_{\text{forearm}}'\operatorname{Var}(\widehat{\beta})\,c_{\text{forearm}} \;=\; c_{\text{hand}}'\operatorname{Var}(\widehat{\beta})\,c_{\text{hand}} \;=\; c_{\text{shin}}'\operatorname{Var}(\widehat{\beta})\,c_{\text{shin}} \;=\; c_{\text{back}}'\operatorname{Var}(\widehat{\beta})\,c_{\text{back}} \]

This is the strongest form of the argument, and it holds regardless of how large or small the site means themselves are. The equality is a property of the design matrix and the assumed covariance, not of the observed data.

The four ingredients

Equality is produced by four conditions acting together, and each one can be removed. First, one pooled residual variance — the model was asked to estimate a single $\sigma^2$ shared by all four sites, so no site is allowed to carry its own noise level. Second, the same participants measured at every site — each person contributes a complete set of four rows, so the site comparisons rest on the same people. Third, the same group sizes at every site — 40 AD and 40 control participants contribute at each site, so $n$ is the same wherever it appears in the formula. Fourth, covariates that are constant within a person — age, sex and phototype take the same value in all four of a participant's rows.

The third ingredient is routinely stated too strongly, including in the sentence above. What the equality requires is that the two group sizes do not change from site to site; it does not require the two groups to be equal to each other, and 30 AD against 50 control at every site would still deliver four identical standard errors, although their common value would no longer be the number the single-$n$ closed form returns.

The fourth ingredient deserves one extra sentence, because it is the one readers usually distrust. Since such a covariate is constant across a participant's four rows, whatever adjustment it imposes is imposed identically at every site; it can move the common standard error up or down, but it cannot move one site's standard error relative to another's. Remove any of the four ingredients, however, and the equality is no longer guaranteed.

One further condition sits underneath all four and is easy to miss, because Spec A satisfies it silently: the marginal covariance has to be compound-symmetric to begin with, which is what a random intercept alone plus one pooled residual variance delivers. Post 5 supplies the counter-example. Add a random slope and the diagonal of $V_i$ becomes a function of time, so the standard errors differ from one occasion to the next even when all four ingredients above hold.

Break the balance and watch

Before the hard part: The cleanest proof that the equality was real is to spoil it deliberately. Below, 12 participants lose their shin measurement, and the shin standard error immediately steps away from the other three. Two ways of computing it are then compared. The naive one treats the shin as if it were a standalone study of 28 patients. The model does better, because those 12 participants still supplied their other three sites, and a mixed model uses a person's other readings to say something about the reading that is missing — much as you would read a patient's other three limbs before deciding what the unrecorded one was likely to show. That borrowing is exactly what the shared offset buys.

The cleanest way to demonstrate a mechanism is to switch it off. Consider the same simulated study with one deliberate defect: 12 participants in the AD group have no usable shin measurement, so that site is estimated from 28 participants instead of 40, while the other three sites keep their full complement. Two calculations follow from that defect, they do not agree with each other, and the disagreement is the most instructive thing in this section.

The naive calculation treats the shin as though it stood alone, mixing the two sample sizes in the balanced formula:

\[ \operatorname{SE}_{\text{naive}}(\widehat{\Delta}_{\text{shin}}) \;\approx\; \sqrt{\frac{\tau^2+\sigma^2}{28} + \frac{\tau^2+\sigma^2}{40}} \;=\; \sqrt{\frac{10.00}{28} + \frac{10.00}{40}} \;=\; \sqrt{0.357+0.250} \;=\; \sqrt{0.607} \;\approx\; 0.78 \]

A likelihood-based fit does better than that, and it does better for the reason this whole series has been building towards. The variance components are shared across sites, so the 12 participants without a shin reading are not lost to the shin mean: the three sites they did provide are tied to the shin through $\tau^2$, and they carry back part of the information the missing rows took away. Writing $n_1 = 28$ for the complete participants, $n_2 = 12$ for the incomplete ones and $N = n_1 + n_2 = 40$, generalised least squares under the assumed $V_i$ gives

\[ \operatorname{Var}(\widehat{\mu}_{\text{shin},\text{AD}}) \;=\; \frac{\tau^2+\sigma^2}{n_1} \;-\; \frac{3\,n_2\,\tau^4}{n_1 N (\sigma^2+3\tau^2)} \;=\; 0.3571 \;-\; 0.0558 \;=\; 0.3013 \]

The subtracted term is precisely the information recovered from the three remaining sites; the 3 in its numerator is their count. The control group is complete and contributes $10.00/40 = 0.25$ as before, so the contrast standard error at the shin is

\[ \operatorname{SE}(\widehat{\Delta}_{\text{shin}}) \;=\; \sqrt{0.3013 + 0.25} \;=\; \sqrt{0.5513} \;\approx\; 0.74 \]

site	participants per group	contrast SE, model-based	contrast SE, naive formula
forearm	40 / 40	0.71	0.71
hand	40 / 40	0.71	0.71
shin	28 / 40	0.74	0.78
back	40 / 40	0.71	0.71

Both columns are closed forms computed from the generating variance components, in g·m⁻²·h⁻¹. They coincide at every site where the design is still balanced, and separate only where it is not.

The column stops repeating the moment the design stops being balanced, which is precisely the evidence that the repetition was never a display bug. Quote 0.74 when you are describing what a fitted model reports, and quote 0.78 only as the naive comparison it is — the balanced formula applied to a site it no longer describes. The gap between the two is worth more than either number on its own, because it is the same phenomenon as the 0.43 against 0.50 further down this post: the shared offset is doing arithmetic work, and here it buys back about half of the extra variance the missing measurements appeared to cost.

Two honest caveats attach to the demonstration. First, both figures are closed forms computed from the generating variance components rather than from estimated ones, so a real fit — with $\widehat{\tau}^{2}$, $\widehat{\sigma}^{2}$ and person-level covariates — will land near them rather than on them. Second, both assume the shin measurements went missing for reasons the model can see. If missingness depends only on recorded information — the participant's group, their covariates, their other three sites — the likelihood-based fit remains valid, and that is the missing-at-random case. If it depends on the unrecorded shin value itself, so that the driest shins are precisely the ones that went unmeasured, then no covariance structure repairs it. That second case requires explicit assumptions and a sensitivity analysis of its own.

The second way to break the equality leaves the balance perfectly intact and attacks the pooled variance instead. In the Spec B simulation of Post 6 the four sites carry different residual variances, so the marginal variance $\tau^2+\sigma_j^2$ becomes 8.00, 9.00, 20.00 and 10.00 rather than a common 10.00 everywhere. The same contrast formula, now carrying a site-specific variance, separates the four standard errors immediately. At the shin, where the marginal variance is 20.00:

\[ \operatorname{SE}(\widehat{\Delta}_{\text{shin}}) \;\approx\; \sqrt{\frac{2(\tau^2+\sigma^2_{\text{shin}})}{n}} \;=\; \sqrt{\frac{2\times 20.00}{40}} \;=\; \sqrt{1.00} \;=\; 1.00 \]

At the back, where the marginal variance is 10.00, the same arithmetic returns $\sqrt{2\times 10.00/40}=\sqrt{0.50}\approx 0.71$, and the forearm and hand — the two quietest sites in that simulation — sit below both. One design, one balanced dataset, four different standard errors.

Here is the uncomfortable half of that observation. Fit a pooled-variance model to Spec B rows and the estimation does not fail, does not warn, and does not refuse. It returns a single $\widehat{\sigma}^{2}$ near the plain average of the four site residual variances — 5.5 in this simulation, because the design is balanced and every site contributes the same number of rows — and it prints four identical standard errors once more. The output looks exactly as tidy as before. Thus the equality of the four numbers tells you which model was fitted, and nothing whatsoever about whether that model deserved to be fitted.

Equal standard errors are not four independent estimates

Before the hard part: What follows is the paired-versus-unpaired argument every clinician already uses. Comparing two sites within the same patient is more precise than comparing two separate groups of patients, because everything that makes that patient run high or low cancels the moment you subtract. The algebra below shows the model doing exactly that, and the giveaway is a smaller standard error for the difference than for either of the means it is built from.

A second objection sometimes follows the first: if the model reports the same uncertainty everywhere, perhaps it is treating the four site means as four separate, unlinked estimates. The model's own output refutes that reading. Consider a within-person site difference — forearm minus back, inside one group:

\[ Y_{i,\text{forearm}} - Y_{i,\text{back}} \;=\; (\mu_{\text{forearm}} - \mu_{\text{back}}) + (b_i - b_i) + (e_{i,\text{forearm}} - e_{i,\text{back}}) \]

The person's offset appears in both terms with the same sign and cancels exactly, leaving only the two residuals. The standard error of that difference therefore drops the between-person variance altogether:

\[ \operatorname{SE}(\widehat{\mu}_{\text{forearm}} - \widehat{\mu}_{\text{back}}) \;=\; \sqrt{\frac{2\sigma^2}{n}} \;=\; \sqrt{\frac{7.50}{40}} \;=\; \sqrt{0.1875} \;\approx\; 0.43 \]

The same number arrives by a second route, which is worth showing because it makes the dependence visible. Each site mean has variance $0.25$, and two site means within the same group covary at $\tau^2/n = 6.25/40 = 0.15625$, because they are computed from the same participants. Then

\[ \operatorname{Var}(\widehat{\mu}_{\text{forearm}} - \widehat{\mu}_{\text{back}}) \;=\; 0.25 + 0.25 - 2(0.15625) \;=\; 0.1875, \qquad \sqrt{0.1875} \approx 0.43 \]

Now compare the two numbers the model reports: 0.43 for the within-person site difference, against 0.50 for either site mean on its own. The difference between two quantities is estimated more precisely than either quantity separately — an arithmetic impossibility if the two means were independent, and the direct fingerprint of the shared offset. A model that treated the four measurements as independent could not produce that number, and this single comparison is usually the fastest way to demonstrate that the random intercept is doing real work.

The symmetric error, and the part most defences get wrong

At this point the temptation is to declare victory, and it should be resisted. Legitimate output does not validate the assumption that produced it. Put the two errors side by side, because they are mirror images and both are false:

1. "Four identical standard errors indicate a bug." False — they are the arithmetic consequence of a balanced design with one pooled residual variance.
2. "Because the standard errors are legitimate output, the pooled-variance assumption must be correct." Equally false — the software computes uncertainty conditional on the covariance structure it was handed, and it will do so just as obediently when that structure is wrong.

The estimator answers the question "what is the uncertainty of this contrast, if the assumed covariance is right?" It has no mechanism for answering "and was it right?" — that question is settled by diagnostics and by refitting, never by the tidiness of the output. This is the point at which a defence either becomes methodologically serious or turns into an argument from software.

When identical standard errors should actually worry you

The equality is expected under the four ingredients. It becomes a reason to look harder when the data contradict the assumption that produced it. Five signals deserve attention. First, markedly different residual spread by unit in the diagnostics — box plots of residuals by site whose widths are visibly not interchangeable. Second, residual-versus-fitted plots showing structured heteroscedasticity, such as a funnel that opens with the fitted value. Third, substantial and unequal missingness across units while the standard errors remain exactly equal, which suggests the equality is being carried by an assumption rather than by the data. Fourth, boundary or singular variance estimates, in which a variance component collapses to zero and the reported structure is not the structure the data supported [1]. Finally, a defensible heteroscedastic alternative that materially changes the confidence intervals or the substantive conclusion — the only one of the five that is decisive, because it demonstrates the assumption is not merely questionable but consequential.

None of these five is a rule that forces a respecification. They are triggers for the analysis described next, and the decision belongs to the diagnostics, not to the aesthetics of the output.

The right way to settle it: a pre-specified sensitivity analysis

There is exactly one answer that ends this conversation properly, and it is not an argument. Refit the model with unit-specific residual variances, holding the fixed-effect structure identical, and report what changed [2].

# Spec A — random intercept, pooled residual variance
library(nlme)
fitA <- lme(tewl ~ site * group + age + sex + phototype,
            random = ~ 1 | id, data = skin, method = "REML")

# Spec B — site-specific residual variance (Post 6)
fitB <- lme(tewl ~ site * group + age + sex + phototype,
            random = ~ 1 | id, weights = varIdent(form = ~ 1 | site), data = skin)

Three procedural points make this a sensitivity analysis rather than a fishing expedition. First, the comparison must use identical fixed effects, because REML likelihoods from different mean structures are not comparable. Second, the analysis should be pre-specified in the protocol or the statistical analysis plan, so that it cannot be read as a response to an unwelcome p-value. Third, a respecification that was not pre-specified is not thereby illegitimate, but it must be labelled for what it is. A structure adopted because the residual diagnostics pointed at it is reported as a post hoc, diagnostics-triggered analysis. A structure adopted because a fixed-effect p-value moved is not a sensitivity analysis in any form, whatever it is called in the manuscript.

Then report honestly. If nothing material moved, a template of this shape may be used, with the blanks filled from your own output:

As a pre-specified sensitivity analysis, the model was refitted with site-specific residual variances and an identical fixed-effect structure. The estimated site × group differences changed by at most [___] g·m⁻²·h⁻¹, the width of every 95% confidence interval changed by less than [___], and the direction and statistical significance of every reported contrast were preserved.

If something did move, say so in the same sentence in which you claim robustness:

As a pre-specified sensitivity analysis, the model was refitted with site-specific residual variances and an identical fixed-effect structure. The principal comparison at [___] was preserved in both magnitude and direction, whereas the comparison at [___] became less precise (95% CI widened from [___] to [___]) and no longer met the conventional threshold of p < 0.05. This secondary comparison is therefore reported as imprecise and hypothesis-generating.

What is not a statistical justification

One argument must be kept out of the methods section entirely. The cost of revising a manuscript, the time already invested in a fitted model, and the inconvenience of regenerating every table are project-management facts. They are real, they legitimately influence what an analysis team decides to do next, and they carry no evidential weight about whether a covariance assumption holds.

Keep the two arguments in separate paragraphs, and never let the second do the work of the first. If the sensitivity analysis shows the conclusion survives, the statistical argument stands on its own and the practical one is unnecessary. If it shows the conclusion does not survive, no amount of practical inconvenience converts that into robustness. A reviewer who detects the two arguments fused into one sentence will, quite reasonably, stop believing the first.

The four-step script

This is the answer to deliver out loud. It takes about a minute.

1. Is it a bug? No. Under a balanced design with one pooled residual variance, the standard error of each site-specific contrast is $\sqrt{2(\tau^2+\sigma^2)/n}$, and there is no site index anywhere in that expression. The four values are equal because the algebra requires it.

2. Why exactly equal? Four conditions hold together: one pooled residual variance, the same participants measured at every site, group sizes that do not change from site to site, and covariates that are constant within a person. Remove any one of them and the equality is no longer guaranteed — with 12 shin measurements missing, for example, that site's contrast SE moves from 0.71 to about 0.74 once the model borrows the other three sites back, and to about 0.78 only if the site is treated in isolation by the naive formula.

3. Does the equality prove the variance assumption is right? No, and this is the important part. The estimator reports uncertainty conditional on the covariance structure it was given; identical standard errors are evidence about the design and the specification, not about their correctness.

4. Does relaxing the assumption overturn the finding? Here is the pre-specified sensitivity analysis with site-specific residual variances, fitted on identical fixed effects — and here is precisely what did and did not change.

Steps 1 and 2 are algebra and may be stated flatly. Steps 3 and 4 are where the credibility is actually earned.

A minimum reporting checklist for a mixed model

A reader should be able to reconstruct your covariance structure from the paper alone. Seven items are usually enough. First, the mean structure, including every interaction that was fitted, not only the ones that reached significance. Second, the random-effects structure and an explicit statement of what the grouping factor is. Third, the residual covariance assumption — pooled, unit-specific, or unstructured — named rather than implied. Fourth, the estimation method (REML or ML) and the degrees-of-freedom approximation used for tests. Fifth, the estimated variance components and the ICC they imply — the values that generated this simulated example are $\tau^2 = 6.25$, $\sigma^2 = 3.75$ and $\rho = 0.625$, and a real REML fit returns estimates near those rather than equal to them, which is exactly why it is the estimates, and not the design values, that belong in the paper. Sixth, the software and version, and the exact model call where journal format allows. Finally, the pre-specified sensitivity analysis of the covariance structure and its result.

A one-paragraph note on degrees of freedom

Denominator degrees of freedom are a genuine open question in mixed models rather than an oversight, and this series has deliberately left them out of scope. In a balanced design with a single grouping factor the common approximations — containment, Satterthwaite, Kenward–Roger — will usually agree closely, and the choice rarely changes a conclusion. With unbalanced data, small cluster counts, or a complicated random structure they can diverge enough to matter, and Kenward–Roger in particular may be preferable because it also adjusts the variance estimate for the uncertainty in the covariance parameters. The reporting rule is simpler than the theory: state which approximation was used, because a t-statistic without its denominator degrees of freedom is not reproducible.

What this post does not license

Three over-readings should be refused explicitly, including the over-strong version of this post's own conclusion.

It does not license the claim that compound symmetry is generally adequate. This series has shown twice that it is not — a random slope destroys it by making the diagonal a function of time, and unequal residual variances destroy the equality of correlations while leaving the covariances untouched. Whether a pooled residual variance is defensible is a question about your diagnostics, your design and your research question, and it must be answered afresh each time.

It does not license treating the closed-form standard errors as what your software will print. The formulas here are exact under the idealised balanced structure of the simulation and approximate everywhere else; a fitted model with estimated variance components, real missingness and person-level covariates will differ, sometimes visibly.

Finally, it does not license the belief that a covariance structure can be selected by watching what happens to the fixed-effect p-values. That procedure invalidates the very inference it is used to defend. Structure is chosen from residual diagnostics, from the design, and from likelihood-based comparison of nested variance models fitted with identical fixed effects.

What to do in your own analysis

Five actions, in the order they are usually needed.

1. Before anything else, plot the residuals by unit. If the spreads look interchangeable, a pooled residual variance may reasonably be retained; if one unit is visibly noisier, that observation belongs in the analysis plan, not in the discussion.
2. Write the covariance structure into the protocol together with the sensitivity analysis that will interrogate it. A structure chosen in advance is a decision; the same structure chosen after seeing the p-values is not.
3. Report an SD and an SE separately, each labelled, and never let a table column be ambiguous between them. Readers cannot recover the distinction from a number alone.
4. Report the variance components and the implied ICC, since they let a reader reconstruct the design effect and judge how much independent information the dataset actually carries.
5. When the two structures disagree, report both. A conclusion that survives a defensible alternative specification is worth more than a conclusion that was never tested, and one that does not survive should be described as what it is.

Key takeaways

• Under a balanced design with one pooled residual variance, the standard error of every unit-specific contrast is the same quantity computed repeatedly, because the expression $\sqrt{2(\tau^2+\sigma^2)/n}$ contains no unit index.
• A raw SD, a residual SD and the SE of an estimated mean are three different quantities, and unequal spread at two units does not imply unequal standard errors for their means.
• Removing any one of the four ingredients — pooled residual variance, complete units per participant, group sizes that do not change across units, within-person-constant covariates — means the equality is no longer guaranteed, as the shin contrast demonstrates: with 12 missing measurements it moves from 0.71 to about 0.74 under a likelihood-based fit, and to about 0.78 under the naive single-site formula that ignores the borrowing.
• Identical standard errors are not four independent estimates: the within-person contrast has SE 0.43 against 0.50 for either mean alone, because the shared offset cancels in the difference.
• Legitimate output never validates the assumption that produced it, so the only real answer to the question is a pre-specified sensitivity analysis with unit-specific residual variances, reported with what did and did not change.

Where the series ends: one number, from the first table to the last column

The series has followed a single quantity from beginning to end. In Post 1 it was visible to the naked eye — one simulated participant sitting above the population profile at all four sites, another sitting below at all four, an offset you could see before any model was fitted. In Post 2 that offset filled a covariance matrix with identical off-diagonals and acquired a name, the intraclass correlation of 0.625. In Post 3 it split the same fitted model into two legitimate readings, independent given the person and correlated across the population. In Post 4 it became a matrix product, $Z_i G Z_i'$, and with it came the map showing that only two things can ever be changed. Posts 5 and 6 changed each of them in turn, and Post 7 refused the decomposition altogether. Here, in the last post, the same mechanism — the offset $b_i$ that one person carries, the variance $\tau^2$ it has across the population, and the correlation $\rho$ it induces between any two of that person's rows — is what makes four standard errors equal and one within-person contrast smaller than either mean it is built from.

That is the whole argument, and it is why the equality in the output column is not a defect. What remains is a habit rather than a formula: state the covariance structure you assumed, show the diagnostics that supported it, and report the sensitivity analysis that tested it. Do that, and the four identical numbers stop being a question you have to survive and become a sentence you can write.

The series in order:

1. The Shared Offset: What a Random Intercept Really Is
2. Compound Symmetry and the ICC: One Offset, One Correlation
3. Conditional or Marginal? Two Questions, One Mixed Model
4. V = ZGZ′ + R: The One Equation Behind Every Mixed Model
5. Random Slopes: When Each Person Carries a Trajectory
6. When Compound Symmetry Is a Lie
7. Population-Averaged Alternatives: GLS, GEE, and Where the Linear Model's Luck Runs Out
8. Four Identical Standard Errors: Defending a Mixed Model in Front of Your Professor — you are here.

References

1. Bates D, Mächler M, Bolker B, Walker S. Fitting linear mixed-effects models using lme4. J Stat Softw. 2015;67(1):1–48.
2. Verbeke G, Molenberghs G. Linear Mixed Models for Longitudinal Data. New York: Springer; 2000.