Power Analysis Exercises in R: 18 Sample Size Problems Solved

Explanation: pwr.t.test() follows the four-knob rule: pass any three of n, d, sig.level, power and leave the fourth as NULL. R solves for the missing one. The output 63.77 means you need 64 patients per arm (always round up: rounding down sacrifices the very power you specified). The NOTE line is easy to miss: total enrollment is 128, not 64.

Explanation: Flipping which argument is NULL flips the question. Here R returns power = 0.478, meaning fewer than half the time a real medium effect would be detected. This is the "post-hoc power" calculation done BEFORE running the study (which is fine and informative). Computing observed-data post-hoc power AFTER the study is a known anti-pattern and not what this exercise does.

Explanation: MDE inverts the design question: instead of "what n do I need to find d?", you ask "given n, what's the smallest d I'd notice?". The answer 0.566 says effects below that magnitude will mostly slip through as non-significant. This framing is honest in stakeholder conversations: it makes the gap between "we found nothing" and "no effect exists" explicit. Pair with the raw effect on the original scale (d × SD).

Explanation: Paired designs use the standard deviation of the per-subject DIFFERENCE, not the raw measurement SD. Because the same subject contributes both observations, within-subject correlation typically cuts that difference-SD substantially, which is why paired designs need far fewer subjects than independent two-sample designs for the same d. Watch for the n is number of pairs note: 68 patients total, not 68 per side.

Explanation: A one-sided alternative is justified ONLY when the direction is decided before any data is seen and the wrong-sign outcome is genuinely uninteresting (here, a worse alloy gets rejected regardless). The one-sided test gains power for free because all of α is on one tail, but the cost is no protection against detecting a real degradation. Make this decision in the protocol, not after looking at pilots, or you bias the inference.

Explanation: Power for unbalanced designs is driven by the harmonic mean of n1 and n2, which is dominated by the smaller arm. 800 vs 200 is roughly equivalent to 320 per arm balanced, so the extra control sessions buy less than you might guess. When you can choose, balanced enrollment is almost always more efficient than 80/20 splits. Use pwr.t2n.test() instead of pwr.t.test() whenever the groups are not equal.

Explanation: A power curve is the right deliverable when stakeholders ask "is n = 100 enough?". pwr.t.test() returns an S3 list, so $power pulls the scalar you need. sapply() works here because the output is a single numeric per call. For ggplot, pipe ex_2_4 into geom_line(aes(n, power)) + geom_hline(yintercept = 0.80, linetype = "dashed") and the answer becomes self-evident.

Explanation: Round up to 45 per group, so 180 total plots. The k argument is the number of groups, not (groups - 1) degrees of freedom: a common slip. Cohen's f is harder to estimate from pilots than d because it requires knowing how group means scatter around the grand mean. If you only have a pilot for two groups, translate that d to f via f = d / 2 when k = 2, then scale up cautiously.

Explanation: Power is 57%: with 25 per group the design is underpowered for a medium effect. The omnibus F detects ANY group difference, but it does NOT tell you which pair differs: that's a separate post-hoc question with its own multiple-comparison correction. If the researcher cares about a specific pair, plan power for that contrast (a two-sample t-test or a planned linear contrast), not the omnibus F.

Explanation: Power for correlation uses Fisher's z (arctanh) transformation, which makes the sampling distribution of r approximately normal. The needed n grows nonlinearly: r = 0.3 needs 85 subjects, r = 0.2 needs about 194, r = 0.1 needs about 781. Small correlations require very large samples. If the literature suggests r ≈ 0.15, a 100-person study is essentially exploratory, not confirmatory.

Explanation: MDE for ANOVA is f ≈ 0.32, which sits between Cohen's medium (0.25) and large (0.40). Plain English: with this design, only between-group spread larger than roughly 30% of the within-group SD will be reliably caught. Smaller true effects will mostly look null. This is the right number to put in the protocol's "limitations" paragraph instead of pretending the study can detect everything.

Explanation: ES.h applies the arcsine transformation: h = 2(asin(√p1) - asin(√p2)). The arcsine variance is stable across the [0,1] range, so the same h has the same statistical meaning whether base rate is 4% or 40%. The result, 6,648 per arm, is much larger than a naive Cohen's d calculation suggests, because a 1-point lift on a 4% base is a tiny absolute effect. This is why low-base-rate A/B tests are notoriously sample-hungry.

Explanation: For chi-square, df is what shifts: a 2×3 table of independence uses (2-1)*(3-1) = 2, a goodness-of-fit with 4 categories uses 4-1 = 3. The N argument is TOTAL observations, not per-cell. Power 62% is borderline; doubling N to 400 lifts it to ≈ 0.91. Effect size w can be computed from a hypothesized contingency table via ES.w1() (one-way) or ES.w2() (two-way) if you don't want to pick a Cohen's convention.

Explanation: ES.w2() compares the supplied joint distribution against the independence model implied by its marginals, returning the effect size for a test of independence. This skips the guesswork of picking Cohen's small/medium/large: the table itself encodes the effect. About 405 respondents are needed. Always check that sum(p_table) == 1 before passing in: ES.w2() will compute even on un-normalized tables and silently return wrong w.

Explanation: pwr.f2.test() returns v (denominator df = n - u - 1). Recover n with u + v + 1. About 83 total observations are needed. Cohen's f² for regression: 0.02 = small, 0.15 = medium, 0.35 = large. To plan power for a SINGLE predictor added to a model with q other predictors, set u = 1 and use f2 = (R²_full - R²_reduced) / (1 - R²_full), which is the partial-effect form.

Explanation: A sensitivity curve answers "what's the smallest d this design can still detect at acceptable power?" by reading the chart at power = 0.80. With n = 60 the design crosses 80% at d ≈ 0.52. Pair it with a plot: ggplot(ex_5_2, aes(d, power)) + geom_line() + geom_hline(yintercept = 0.8, linetype = "dashed"). Submitting both the sample-size curve (fixed d, varying n) and the sensitivity curve (fixed n, varying d) is the gold standard for power sections in proposals.

Explanation: Bonferroni's tax: shrinking α from 0.05 to 0.005 drops per-test power from 56% to 41%. Multiple-testing burden is invisible if you only plan the primary endpoint, then surprise-add secondaries. Plan it up front: either preregister a smaller set of confirmatory endpoints, switch to a less conservative method (Holm, BH-FDR), or budget for the larger n needed under Bonferroni. Bonferroni is conservative when tests are correlated, so simulation-based adjustments can outperform it.

Explanation: Monte Carlo estimates of power match pwr.t.test() because both test the same statistic on the same population. The real value of simulation is for SCENARIOS pwr cannot handle: heavy-tailed data, mixed-effects models, custom Bayesian decision rules, conditional stopping. Standard error on the simulated power estimate is roughly sqrt(p(1-p)/n_sim), so 2000 reps gives ±1.1%. Bump to 10,000 reps for tighter intervals or when the test is computationally cheap.