In 2013, Katherine Button and colleagues analysed 730 neuroscience studies published in top journals and found that the median statistical power — the probability of detecting a true effect — was just 20%. Four out of five real effects in those fields were being systematically missed, not because they were absent, but because the studies were too small to see them. The paper, published in Nature Reviews Neuroscience, ignited a debate that has since reshaped how clinical and psychological research is designed and evaluated. The problem was not unique to neuroscience: a Cochrane review of 215 meta-analyses found that the majority of trials included were substantially underpowered for their primary outcomes. Underpowering is not merely a statistical technicality — it generates false negatives that withhold effective treatments from patients, inflates published effect sizes through publication bias, and wastes research resources on studies that cannot produce definitive conclusions. Statistical power analysis is the solution: the method for determining, before data collection begins, whether a planned study is capable of detecting the effect it is designed to find.
Type I and Type II Errors: The Decision Framework
Every hypothesis test produces one of four outcomes depending on whether the null hypothesis is truly true or false, and whether the test rejects it or not. Understanding these four cells is prerequisite to understanding power.
✅ Correct Rejection Absent
p ≥ α (Do not reject H₀)
True negative. You correctly conclude no effect exists. Probability = 1 − α = 0.95.
❌ Type II Error (β)
p ≥ α (Do not reject H₀) — FALSE NEGATIVE
Miss a real effect. Conventional β = 0.20 (power = 0.80). The study was too small to see what was there.
❌ Type I Error (α)
p < α (Reject H₀) — FALSE POSITIVE
Detect an effect that does not exist. Conventional α = 0.05. The significance threshold directly controls this probability.
✅ True Positive (Power)
p < α (Reject H₀)
Correctly detect a real effect. Power = 1 − β. Conventional target: 0.80 (80%). This is what well-designed studies maximise.
The critical insight from this matrix: Type I and Type II errors trade off against each other when sample size is fixed. Making the significance threshold more stringent (lowering α from 0.05 to 0.01) reduces false positives but simultaneously increases false negatives (reduces power). The only way to reduce both errors simultaneously is to increase the sample size. Power analysis quantifies exactly how large the sample must be to achieve an acceptable balance between these two error rates for a given expected effect size.
What is Statistical Power?
Statistical power is the probability that a study will produce a statistically significant result, given that the true effect in the population is at least as large as the effect size assumed in the power calculation. Formally:
Power is not a fixed property of a statistical test — it depends on the specific effect size you are trying to detect, the sample size available, the significance level chosen, and the variability of the outcome. A study can have 90% power to detect a large effect (d = 0.80) but only 25% power to detect a small one (d = 0.20) with the same sample size. This is why the expected effect size — specifically, the minimum clinically important difference (MCID) — must be specified before sample size can be calculated.
The power-sample size intuition: Power increases with the square root of sample size for mean differences. To double your power (from 40% to 80%), you need approximately four times the sample size — not twice. This nonlinear relationship means that very small underpowered studies (n = 10/group) cannot be rescued by modest increases in recruitment; a fundamental redesign is required.
The Four Determinants of Power
These four factors are mathematically linked — specifying any three determines the fourth. Power analysis is the process of solving for one of them (usually sample size) given the other three.
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1. Effect Size
The magnitude of the true population effect you expect to find and need to detect — expressed as Cohen’s d, OR, RR, Cramér’s V, or correlation r. Larger effects are easier to detect and require fewer participants.
↑ Larger effect → more power (same n)
👥
2. Sample Size (n)
The total number of participants (or observations per group). Power increases with n, but not linearly — quadrupling n roughly doubles detectable effect size. The sample size is what the power calculation solves for.
↑ Larger n → more power (same effect)
α
3. Significance Level (α)
The Type I error threshold. A more lenient α (e.g., 0.10 vs 0.05) increases power because the critical value decreases — but at the cost of more false positives. Rarely changed from 0.05 in practice.
↑ More lenient α → more power (same n)
📈
4. Outcome Variability (SD)
The standard deviation (or variance) of the primary outcome in the target population. Lower variability increases the signal-to-noise ratio and improves power. Can be reduced through better measurement, tighter eligibility criteria, or covariate adjustment (ANCOVA).
↓ Lower SD → more power (same n and effect)
The z-approximation formulas below are the basis of most sample size calculators. G*Power 3.1 (free, Windows/Mac) implements exact versions for all major test families; the formulas here give very close approximations and are directly interpretable.
Independent t-Test (Two-Group Mean Comparison)
Chi-Square Test of Association
Pearson / Spearman Correlation
Power for Common Scenarios at α = 0.05 (Two-Tailed)
| Effect Size | Category | n/group (80% power) | n/group (90% power) | Power with n=20/group |
|---|
| d = 0.20 | Small | 394 | 527 |
9% |
| d = 0.35 | Small-medium | 131 | 175 |
18% |
| d = 0.50 | Medium | 64 | 86 |
34% |
| d = 0.65 | Medium-large | 39 | 52 |
52% |
| d = 0.80 | Large | 26 | 34 |
69% |
| d = 1.00 | Very large | 17 | 22 |
86% |
The n = 20 trap: Many student research projects enrol 20–30 participants per group because of convenience — the number of patients available in a ward, a semester’s recruitment window, or an archive’s accessible records. The table above shows that n = 20/group provides only 34% power to detect a medium effect (d = 0.50). Two out of three real medium effects will be missed. At d = 0.35 (a common realistic expectation in clinical research), power is only 18%. These studies almost inevitably produce non-significant results that are falsely interpreted as evidence of no effect.
Clinical Examples
1
RCT of a New Antihypertensive: A Priori Sample Size Calculation
A clinical pharmacologist is designing an RCT to evaluate a new antihypertensive agent versus placebo in adults with stage 1 hypertension. The primary outcome is systolic blood pressure (SBP) reduction at 12 weeks. A pilot study in 20 patients showed a mean SBP difference of 7.2 mmHg (SD 14.1 mmHg) between the groups. The clinical team agrees that a minimum clinically important difference of 7 mmHg justifies proceeding to a larger trial. Conventional α = 0.05, two-tailed; target power 80%. A 15% dropout rate is anticipated.
7 mmHg
MCID (target difference)
14 mmHg
Expected SD (from pilot)
Step 1 — Compute Cohen's d
d = MCID / SD = 7 / 14 = 0.500
Step 2 — Apply t-Test Sample Size Formula
z_α/2 = 1.960 (α = 0.05, two-tailed)
z_β = 0.842 (power = 0.80)
(z_α/2 + z_β)² = (1.960 + 0.842)² = (2.802)² = 7.851
n per group = 2 × 7.851 / d²
= 2 × 7.851 / 0.250
= 15.702 / 0.250
= 62.8 → 64 per group (round up)
Total (without dropout): 64 × 2 = 128 participants
Step 3 — Adjust for 15% Anticipated Dropout
n_enrol = n_required / (1 − dropout rate)
= 64 / (1 − 0.15) = 64 / 0.85 = 75.3 → enroll 76 per group
Total enrollment target: 76 × 2 = 152 participants
Step 4 — Verify with Power = 90% (sensitivity)
z_β = 1.282 for 90% power
n = 2 × (1.960 + 1.282)² / 0.250 = 2 × 10.510 / 0.250 = 84.1 → 85/group → 200 enrolled
[Use 80% power for feasibility; 90% for high-stakes primary outcome]
Step 5 — Minimum Detectable Effect at n = 64/group
MDE_d = √(2 × 7.851 / 64) = √(0.2453) = 0.495 → ~7.0 mmHg
[Confirms the calculation is consistent]
Enrol 76 participants per group (152 total) to achieve 80% power to detect a 7 mmHg SBP difference (d = 0.50) at α = 0.05 two-tailed, after 15% dropout allowance. Calculated using G*Power 3.1 (t-tests — Means: Difference between two independent means, two-tailed).
Key reporting principle: This calculation appears verbatim in the Methods section. Every number is justified: the 7 mmHg MCID comes from established clinical guidelines for meaningful SBP reduction; the SD = 14 mmHg comes from the pilot study (cited); 80% power is the conventional minimum; the dropout rate of 15% reflects historical attrition in this unit’s trials. Reviewers and ethics committees expect this level of justification. Do not use Cohen’s conventional ‘medium’ as the effect size without clinical justification — ‘We assumed a medium effect’ is not scientifically acceptable.
2
Retrospective Chart Review: Diagnosing an Underpowered Study
A medical student’s thesis compares anxiety scores (GAD-7) between diabetic and non-diabetic outpatients. Due to chart availability, n = 18 per group were retrieved. The t-test returned p = 0.283 — not significant. The student concludes: “There was no significant difference in anxiety between diabetic and non-diabetic patients.” Is this conclusion valid?
12.4
Diabetic mean GAD-7 (SD 6.1)
10.1
Control mean GAD-7 (SD 5.8)
Step 1 — Compute the Observed Effect Size
S_p = √[((17×6.1²) + (17×5.8²)) / 34]
= √[(632.57 + 572.12) / 34]
= √[1204.69 / 34] = √35.43 = 5.95
Observed d = (12.4 − 10.1) / 5.95 = 2.3 / 5.95 = 0.387
Step 2 — Compute Achieved Power for Observed d at n=18/group
Non-central t approximation:
λ = d × √(n/2) = 0.387 × √9 = 0.387 × 3 = 1.161
Critical t (df=34, α=0.05, two-tailed) ≈ 2.032
Power ≈ P(t > 2.032 − 1.161) + P(t < −2.032 − 1.161)
≈ P(t > 0.871) [using central approximation] ≈ 0.20
Achieved power: approximately 20% (only 1 in 5 chance of detection)
Step 3 — Compute n Required to Achieve 80% Power for d=0.387
n = 2 × 7.851 / d² = 2 × 7.851 / 0.150 = 104.7 → 53 per group required
Total needed: 106 participants — the study enrolled 36 (34% of target)
Step 4 — Minimum Detectable Effect at n=18/group, Power=80%
MDE_d = √(2 × 7.851 / 18) = √(0.872) = 0.934
[To have 80% power with n=18/group, the true d would need to be ≥ 0.93 — very large]
Conclusion: Was the Study Adequately Powered?
Target n (for d=0.387 at 80% power): 53/group
Enrolled n: 18/group — only 34% of what was needed
Power achieved: ~20%
Type II error probability: ~80%
The study was critically underpowered (achieved power ≈ 20% for the observed effect size of d = 0.39). The non-significant result (p = 0.283) cannot be interpreted as evidence of no difference. The study needed approximately 53 participants per group (106 total) to have adequate power; only 18 per group were enrolled. The correct conclusion is: “This underpowered study was unable to confirm or exclude a clinically relevant difference in GAD-7 scores between groups.”
The danger of the underpowered negative result: The student’s original conclusion — “no significant difference” — implies equivalence, which this study design cannot establish. The 95% CI for the mean difference (2.3 points) likely spans from −2 to +6.6 — consistent with both no effect and a large clinically meaningful difference. An adequately powered equivalence study would require a formally defined equivalence margin and a different statistical test (TOST — Two One-Sided Tests). Retrospective studies with convenience samples should always have post-design power evaluated — not to report observed power, but to contextualise what effects could or could not have been detected with that sample.
3
Chi-Square Study: Sample Size for a Categorical Association
A surgical researcher wants to study the association between patient smoking status (smoker / non-smoker) and postoperative complication rate (complication / no complication) after elective colorectal surgery. Based on the literature, Cramér’s V ≈ 0.25 is expected. Target: α = 0.05, power = 0.80. An additional 20% recruitment buffer is planned for consent withdrawals.
V = 0.25
Expected Cramér’s V
Step 1 — Apply Chi-Square Sample Size Formula
w = V = 0.25 (for a 2×2 table, w = Cramér's V)
(z_α/2 + z_β)² = (1.960 + 0.842)² = 7.851
N_total = (z_α/2 + z_β)² / w²
= 7.851 / (0.25)²
= 7.851 / 0.0625
= 125.6 → 126 total participants
Step 2 — Verify with G*Power Logic (exact chi-square)
G*Power: χ² tests — Goodness-of-fit tests: contingency tables
Input: w = 0.25, α = 0.05, power = 0.80, df = 1
Output: N = 128 (exact; z-approximation gives 126 — very close)
Step 3 — Adjust for 20% Withdrawal
N_enrol = 128 / 0.80 = 160 total participants to recruit
Step 4 — Sensitivity: What V Is Detectable at N=128?
MDE_V = √(7.851 / 128) = √0.0614 = 0.248 → V ≈ 0.25 ✓
Step 5 — Power at V=0.15 (smaller true association)
w = 0.15; power ≈ (z_α/2 + z_β = √(N × w²) − z_α/2)
√(128 × 0.0225) = √2.88 = 1.697
Power ≈ Φ(1.697 − 1.960) = Φ(−0.263) ≈ 40%
[If true V = 0.15, this study has only 40% power — consider sensitivity analysis]
Enrol 160 participants total (128 required for 80% power at V = 0.25, adjusted for 20% withdrawal). Calculated using G*Power 3.1 (χ² tests — Goodness-of-fit tests: contingency tables, df = 1). The study is powered to detect a small-to-medium association; a sensitivity analysis shows only 40% power if the true association is V = 0.15.
Sensitivity analysis is not optional: The expected effect size in this calculation came from prior literature — but published Cramér’s V estimates are often inflated by the Winner’s Curse (only studies with larger-than-true effects pass significance thresholds and get published). Running a sensitivity analysis across a range of plausible V values (0.15, 0.20, 0.25) and presenting the corresponding required sample sizes gives the research team a realistic range to plan recruitment around. If the budget permits only 90 participants, the team should know in advance that this study can only reliably detect associations of V ≥ 0.30 — and adjust the research question accordingly.
The Post-Hoc Power Trap
One of the most common and consequential misuses of power analysis is conducting a post-hoc (observed, retrospective) power analysis after a non-significant result and reporting the result as evidence that the study was powered. This practice is mathematically circular and scientifically meaningless.
Why post-hoc observed power is uninformative: Observed power is calculated using the observed effect size from the same data that produced the p-value. Since observed power is a monotone function of p, a non-significant result (p = 0.28) will always produce low observed power (e.g., 22%) — and a significant result (p = 0.03) will always produce high observed power. The two statistics carry identical information. Reporting “post-hoc power was 22%” alongside “p = 0.28” adds nothing. The American Psychological Association and the BMJ style guide both explicitly warn against this practice.
What to report instead when a study produces a non-significant result:
- The a priori power calculation from the Methods section — this shows the study was designed for adequate power to detect the pre-specified MCID.
- The observed effect size with 95% CI — the confidence interval shows what effect magnitudes are consistent with the data. A wide CI encompassing both clinically meaningful and trivial effects indicates imprecision, not evidence of no effect.
- The minimum detectable effect (MDE) — the smallest effect that could have been detected at 80% power given the actual sample size. If the MDE is larger than the MCID, the study was underpowered for what was clinically relevant.
- A statement of inconclusiveness — “this study was unable to confirm or exclude a clinically meaningful difference; a larger powered study is warranted” is the honest conclusion from an underpowered non-significant result.
Thesis Writing Recommendations
In the Statistical Analysis Section
The power calculation belongs in the Statistical Analysis subsection of Methods, not in the Discussion or as a footnote. Every element of the calculation must be justified, not merely stated. Reviewers and examiners will ask: where did the expected effect size come from? Why did you choose 80% vs 90% power? Why a two-tailed test?
Model Power Analysis Paragraph — Two-Group RCT
“Sample size was calculated to detect a minimum clinically important difference of 7 mmHg in systolic blood pressure (SD 14 mmHg; d = 0.50), derived from published MCID estimates for antihypertensive interventions in stage 1 hypertension (Smith et al., 2022). Assuming a two-tailed significance level of α = 0.05 and 80% power (β = 0.20), 64 participants per group were required. Accounting for an anticipated 15% dropout rate based on historical attrition in our unit, 76 participants per group (152 total) were enrolled. Sample size was calculated using G*Power 3.1 (t-tests: Difference between two independent means, two-tailed; Faul et al., 2007).”
Model Sentence When Target N Was Not Reached
“The study enrolled 54 of the planned 128 participants (42% of target) due to early closure during COVID-19 restrictions. Post-hoc sensitivity analysis indicates that with n = 27 per group, the study had 80% power to detect a minimum effect of d = 0.77 — larger than the pre-specified MCID of d = 0.50 (7 mmHg). The non-significant primary outcome result (p = 0.14, d_obs = 0.43, 95% CI: −0.11, 0.97) is therefore inconclusive and should not be interpreted as evidence of no clinically meaningful effect.”
G*Power Citation
Always cite the software and version used. The standard reference for G*Power 3.1 is: Faul, F., Erdfelder, E., Lang, A.-G., & Buchner, A. (2007). G*Power 3: A flexible statistical power analysis program for the social, behavioral, and biomedical sciences. Behavior Research Methods, 39(2), 175–191.
Common Mistakes
Mistake 1: Using Cohen’s ‘Medium Effect’ Without Clinical Justification
The most prevalent error in student power calculations: “We assumed a medium effect size (d = 0.50) as per Cohen (1988).” Cohen himself stated these thresholds were “conventions of convenience” for when no domain knowledge was available — they were explicitly not intended as defaults for clinical research. A d = 0.50 in your specific clinical context may correspond to an effect far too small or far too large to be clinically relevant.
Fix: Base your expected effect size on (1) the MCID for your primary outcome; (2) pilot data from your own population; or (3) systematic review estimates from comparable populations, adjusted downward by ~20–30% for the Winner’s Curse. Document the source explicitly.
Mistake 2: Conducting Post-Hoc Power Analysis on a Non-Significant Result
Running a power calculation after a failed study using the observed effect size, then reporting “post-hoc power was 23%, suggesting the study was underpowered,” is mathematically circular. Observed power is entirely determined by the p-value — they carry the same information. Journals including the BMJ and JAMA explicitly state that post-hoc power should not be reported as a primary finding.
Fix: Report the a priori power from the Methods. For the non-significant result: report the observed effect size with 95% CI, the minimum detectable effect at the actual n, and a clear statement of inconclusiveness. Never use observed power to “explain” a non-significant result.
Mistake 3: Failing to Account for Dropout in the Target Sample Size
A power calculation for 64 participants per group produces a target for the analysable sample — the participants who complete the study and contribute data to the primary analysis. If 20% of enrolled participants drop out, the actual analysable n is 80% of enrollment. Many thesis students confuse enrollment targets with analysis targets and under-recruit, producing underpowered analyses.
Fix: Always adjust the analysis target upward: n_enrol = n_analysis / (1 − dropout rate). For clinical trials, estimate dropout from historical attrition in similar studies in your unit. For cross-sectional studies, account for data quality issues (missing data, exclusion criteria violations).
Mistake 4: One-Tailed Testing to Inflate Power
Using a one-tailed test reduces the critical value (e.g., from z = 1.96 to z = 1.645 for α = 0.05), which increases power and reduces required sample size by approximately 20–25%. Some researchers exploit this by specifying a one-tailed test purely to lower recruitment targets, even when the research question is genuinely bidirectional. A one-tailed test is scientifically justified only when: (a) an effect in the opposite direction would be clinically impossible or irrelevant, and (b) this was pre-registered before data collection.
Fix: Default to two-tailed tests for all clinical comparisons. Use one-tailed tests only when the pre-registered hypothesis genuinely specifies directionality and an effect in the opposite direction is neither clinically plausible nor of interest. State the rationale explicitly and pre-register the analysis plan.
Mistake 5: Inflated Effect Size Estimates from Pilot Studies
Pilot studies of 10–20 participants are routinely used to estimate effect sizes for power calculations in larger trials. However, effect size estimates from small samples are highly variable and systematically inflated due to the Winner’s Curse — only the most extreme (largest) effects from small-sample exploratory work receive follow-up funding. Using d = 0.85 from a pilot of n = 12 to plan a full trial expecting d = 0.85 will produce a substantially underpowered study if the true population effect is d = 0.50.
Fix: Apply a conservative discount of 25–50% to effect size estimates from pilot studies when planning the full trial. Use the lower bound of the 95% CI from the pilot as a conservative planning estimate. Alternatively, plan on a range of effect sizes and present power for each in a sensitivity table.
Mistake 6: Not Revisiting the Power Calculation After Protocol Amendments
Studies frequently change their primary outcome mid-protocol — switching from a continuous to a binary endpoint, adding a co-primary outcome, or changing the measurement instrument. Any change to the primary outcome measurement changes the expected effect size, variability, and therefore the required sample size. Researchers often do not recalculate after amendments, leaving the study mismatched between its power calculation and its actual analysis.
Fix: Whenever the primary outcome or its measurement changes, recalculate sample size from scratch using the new outcome’s MCID and expected variance. Document the revision formally (ethics amendment if required). In multi-arm studies, account for multiple comparisons — each additional arm or primary outcome requires a Bonferroni-adjusted α and a larger sample.
Scientific Reporting Standards
- CONSORT 2010 (Item 7a): Requires explicit reporting of “how sample size was determined,” including: the primary outcome, the expected effect size and its source, α, power, and the resulting sample size. If the study was not RCT but used a power calculation, STROBE and TREND make equivalent recommendations.
- SPIRIT 2013 (Item 14): For trial protocols, requires the full sample size justification with all assumptions. Effect size, variability estimate, α, power, dropout adjustment, and the formula or software used must all be documented.
- ICH E9 (FDA/EMA): Recommends 90% power for Phase III RCT primary outcomes with clinical implications (mortality, major morbidity). The 80% convention is acceptable for exploratory and secondary outcomes.
- APA 7th Edition (Section 3.10): Authors must justify sample size in quantitative research reports; power analysis is explicitly listed as acceptable justification. Observed power is discouraged as the justification for a completed study’s adequacy.
- BMJ Statistics Notes: Several BMJ Stats Notes columns (Altman & Bland; Goodman & Berlin) explicitly address the misuse of post-hoc power analysis and recommend reporting confidence intervals for effect sizes instead.
Practical Guidance
Use G*Power 3.1 — It’s Free and Comprehensive
G*Power covers power analysis for over 50 statistical tests — t-tests, ANOVA, chi-square, correlation, regression, logistic regression, Mann-Whitney, Wilcoxon, and more. Download from gpower.hhu.de. Always specify: (1) test family; (2) statistical test; (3) type of analysis (a priori, post-hoc, or sensitivity); (4) one-tailed or two-tailed. The output window gives you a power curve plot, the calculated n, and the non-centrality parameter — screenshot it for your thesis appendix.
Build a Sensitivity Table for Your Power Analysis
Rather than reporting a single power calculation for one assumed effect size, present a 3×3 sensitivity table showing required sample sizes (or achieved power) across a range of plausible effect sizes (e.g., d = 0.35, 0.50, 0.65) and power levels (70%, 80%, 90%). This transparently communicates the study’s capacity across a range of assumptions and demonstrates sophisticated understanding of power to examiners and reviewers.
Increase Power Without Adding Participants
When recruitment is constrained, four strategies can improve power without increasing n: (1) Switch to a paired or repeated-measures design if feasible — pairing eliminates between-subject variance and can double effective power. (2) Add ANCOVA covariate adjustment for a strong baseline measure of the outcome — can reduce residual variance by 30–50%. (3) Tighten eligibility criteria to reduce outcome variability (at the cost of generalisability). (4) Increase measurement precision — use validated, reliable instruments with lower measurement error.
Pre-Register Your Power Calculation
Register your power calculation, expected effect size, and analysis plan on ClinicalTrials.gov (for interventional studies) or the OSF (for observational research) before data collection begins. Pre-registration creates an immutable record that the power analysis was prospective — not reverse-engineered from the data — and significantly strengthens the credibility of both significant and non-significant results. Ethics committees increasingly require registration as a condition of approval for studies involving human participants.
Plan for Interim Analyses in Long-Running Trials
If your RCT includes one or more interim analyses (e.g., a pre-planned safety review at 50% enrollment), the overall Type I error must be partitioned across the planned tests using an alpha-spending function (O’Brien-Fleming or Pocock boundaries). Failing to account for interim analyses inflates the Type I error rate above 0.05. The required total sample size also increases modestly to preserve overall power after the interim look. G*Power does not handle group sequential designs — use EAST, PASS, or the R package gsDesign.
Report the Minimum Detectable Effect for Every Study
Regardless of whether the study was adequately powered, always calculate and report the minimum detectable effect (MDE): the smallest effect the study could have detected at 80% power with its actual sample size. The MDE provides context for interpreting non-significant results — if MDE = d = 0.93 and the MCID is d = 0.50, readers immediately see that the study was too small to address the clinical question. MDE is the honest alternative to the misleading ‘observed power’ calculation.
Frequently Asked Questions
What is statistical power and why does it matter? +
Statistical power is the probability that a study will detect a true effect — a real difference, association, or relationship — when one actually exists in the population. Power = 1 − β, where β is the Type II error rate (false negative probability). A study with 80% power has an 80% chance of producing a statistically significant result, given that the true effect is as large as assumed. Power matters because underpowered studies routinely miss genuine clinical effects, wasting resources, misleading clinicians, and contributing to the replication crisis. A non-significant result from an underpowered study cannot be interpreted as evidence of no effect — it may simply have been too small to see what was there.
What is the difference between Type I and Type II errors? +
A Type I error (α, false positive) occurs when you reject the null hypothesis when it is actually true — detecting an effect that does not exist. The significance threshold α = 0.05 means you accept a 5% probability of this error. A Type II error (β, false negative) occurs when you fail to reject the null hypothesis when it is actually false — missing a real effect. The conventional β = 0.20 (power = 0.80) means you accept a 20% probability of missing a true effect. Lowering α reduces Type I errors but increases Type II errors (reduces power) at fixed n. The only way to reduce both simultaneously is to increase sample size. The relative clinical cost of each error type should inform which takes priority in study design.
What are the four determinants of statistical power? +
Power is determined by: (1) Effect size — larger true effects are easier to detect; a larger expected effect means fewer participants are needed for the same power. (2) Sample size — more participants increase power, but not linearly; power grows with the square root of n for mean differences. (3) Significance level (α) — a more lenient threshold increases power but also increases false positives. (4) Outcome variability (SD) — lower variance increases the signal-to-noise ratio and improves power. These four factors are mathematically coupled: specifying any three determines the fourth. Power analysis solves for sample size when effect size, α, and target power are given.
How do I calculate sample size for a two-group comparison? +
For an independent t-test (two continuous group means): n per group = 2 × (zα/2 + zβ)² / d². For α = 0.05 (z = 1.96) and 80% power (z = 0.842): n = 2 × 7.851 / d² = 15.70 / d². For d = 0.50: n = 15.70 / 0.25 = 62.8 → 64 per group. Always add a dropout adjustment: n_enrol = n_required / (1 − dropout rate). For d = 0.50, 15% dropout: 64 / 0.85 = 76 per group (152 total). G*Power 3.1 (free) replicates this calculation and handles all major test types.
What is post-hoc power analysis and why should I avoid it? +
Post-hoc (observed) power calculates the power a completed study would have had to detect the observed effect size. It is mathematically circular: a non-significant result will always produce low observed power; a significant result will always produce high observed power — they carry identical information. Reporting “post-hoc power was 21%” after p = 0.24 adds nothing. Instead, report: (1) the a priori power calculation from Methods; (2) the observed effect size with 95% CI; (3) the minimum detectable effect at the actual n. These three convey meaningful information about the study’s capacity and the precision of the result.
What is an underpowered study and what are its consequences? +
An underpowered study has insufficient sample size to detect the expected clinically meaningful effect with adequate probability (≤ 80%). Consequences: (1) False negatives — real effects go undetected and are erroneously reported as ‘no significant difference.’ (2) Winner’s Curse — only the most inflated estimates cross the significance threshold and get published, inflating the literature’s average effect size. (3) Research waste — resources and patient participation used without producing definitive evidence. (4) Misleading clinical decisions — guideline recommendations based on underpowered negative trials may deny patients effective treatments. Button et al. (Nature Reviews Neuroscience, 2013) estimated median neuroscience study power at 20%.
What power level should I target for my study? +
Minimum convention is 80% power (β = 0.20), established by Cohen (1988) and standard for most clinical research. Higher targets are warranted in specific contexts: (1) RCTs with mortality or major morbidity as primary outcomes — FDA/ICH E9 recommends 90% power (β = 0.10). (2) When Type II errors are particularly costly (a missed effective treatment for a serious disease). (3) When the study is definitive (pivotal trial) rather than exploratory. Moving from 80% to 90% power increases required n by approximately 27% (zβ changes from 0.842 to 1.282). Always justify and pre-specify your target power in the Methods.
How do I specify the expected effect size for a power calculation? +
The expected effect size should be the minimum clinically important difference (MCID), converted to a standardised effect size. Sources in order of reliability: (1) Published MCID for your primary outcome (e.g., PHQ-9 MCID = 5 points; FIM MCID = 22 points; SBP MCID = 5–10 mmHg). Convert to d = MCID / SD. (2) Pilot data in the same population — but apply a 25–40% discount for likely inflation. (3) Published literature — from comparable populations and outcomes; adjust downward for the Winner’s Curse. Avoid ‘medium effect (d = 0.50) per Cohen (1988)’ without clinical justification — reviewers and ethics committees will challenge it.
How should I report power analysis in a thesis or paper? +
In the Statistical Analysis subsection of Methods, include: (1) the primary outcome and MCID; (2) the expected effect size and its source; (3) α and whether one- or two-tailed; (4) target power and justification; (5) calculated n per group and total; (6) dropout adjustment and adjusted enrollment target; (7) software used. Model sentence: “Assuming a minimum clinically important SBP difference of 7 mmHg (SD 14 mmHg, d = 0.50), α = 0.05 two-tailed, and 80% power, 64 participants per group were required. Accounting for 15% dropout, 76 per group (152 total) were enrolled. Calculated using G*Power 3.1 (Faul et al., 2007).”
Can I still publish a study that didn’t reach its target sample size? +
Yes, with full transparency. Report: (1) the a priori target and the achieved n; (2) the power actually achieved at the achieved n for the pre-specified effect size (not observed power); (3) the minimum detectable effect at the achieved n and whether the observed effect was above or below it; (4) careful framing of non-significant results — ‘This underpowered study was unable to confirm or exclude a clinically meaningful difference’ rather than ‘no significant difference was found.’ Do not interpret underpowered non-significant results as evidence of equivalence — that conclusion requires a formally powered equivalence or non-inferiority design with pre-specified margins.
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