Drive the four levers yourself and watch what sample size actually buys
You now know the four levers: sample size, effect size, alpha, variability. What you don't have yet is a feel for the exchange rates — how much power one more patient buys, how brutally the cost climbs as the effect shrinks, why "we'll just enroll 50 and see" almost never works.
This lesson gives you a live power calculator. You'll set up studies, break them, and fix them. By the end, when someone proposes detecting a 5% difference with 60 patients, you'll feel the wrongness before you compute it.
The calculator uses the standard normal-approximation formulas — the same math inside most power software. It's built for intuition and journal-club sanity checks. For an actual protocol, confirm with dedicated software or a statistician (they'll add refinements like continuity corrections that nudge n slightly upward).
Every two-arm sample size calculation needs the same four ingredients.
For a binary outcome: the control event rate and the treatment event rate you're designing to detect (e.g., SSI of 20% vs 10%). For a continuous outcome: the difference in means and the outcome's standard deviation (e.g., 2 days shorter stay, SD 5 days). This pair encodes both the effect size and the variability levers.
Almost always 0.05, two-sided. Stricter alpha (0.01) buys fewer false alarms at the cost of more patients.
80% is the conventional floor; 90% is increasingly expected for definitive trials. The step from 80% to 90% costs about a third more patients — you'll verify this yourself in a minute.
The formula's n is the number of analyzable patients. Real studies lose people to dropout, crossover, and missing data — so inflate: enrolling n / (1 − dropout rate) protects the analysis (e.g., need 200, expect 20% attrition → enroll 250). Section 4 covers the other adjustments that show up in real protocols.
That's the whole recipe. When a methods section says "assuming X% vs Y%, alpha 0.05 and 80% power, we required N patients per arm," you now know each ingredient — and after Lesson 2, you know which one to interrogate.
Two-arm comparison, two-sided test. Drag the sliders and watch power respond.
The formula is the floor. Four adjustments separate a textbook calculation from a fundable one.
Divide, don't multiply: needing 200 analyzable patients with 20% expected attrition means enrolling 200/0.8 = 250, not 200 × 1.2 = 240. The difference grows with the dropout rate, and using the wrong version is a surprisingly common protocol error.
For time-to-event analyses (Module 4), power comes from the number of events — deaths, amputations, occlusions — not the number of enrolled patients. A 500-patient trial with 30 events is a 30-event trial. This is why low-event-rate trials run for years and why "we'll just follow them longer" is a legitimate power strategy.
Same logic underlies logistic regression's events-per-variable rule from Module 5 — in rare-outcome studies, events are the real currency everywhere.
2:1 randomization (often used when patients or surgeons prefer the new treatment) costs power: for the same total n, 2:1 needs about 12% more patients than 1:1 to reach the same power. Beyond 3:1 the penalty climbs steeply. Balanced arms are the efficient default; deviations need a reason.
Each additional primary endpoint or interim analysis spends alpha (more chances for a false alarm), so honest designs split the alpha or use formal spending rules — and that stricter effective alpha raises the required n. A power statement that names one endpoint while the abstract celebrates a different one is a Module 1 red flag with a Module 6 explanation.
Reading order for any power paragraph: ingredients (rates, delta, alpha, power) → arithmetic (does the n check out?) → adjustments (dropout? events? allocation?) → and finally, did the analysis actually use the endpoint the study was powered for?
Use the calculator below to answer — these are real design problems, not memory questions.
Module 6 - Lesson 3 complete
Next lesson: The Underpowered Study Problem — what to do (and what never to claim) when the sample size is fixed by reality, plus the post-hoc power fallacy that reviewers keep requesting anyway.