Common Statistical Pitfalls

Use the estimand, sampling design, and assumptions to judge an analysis; the examples below are illustrative. Primary guidance is linked in review_sources.md.

P-Value Misinterpretations

Pitfall 1: P-Value = Probability Hypothesis is True

Misconception: p = .05 means 5% chance the null hypothesis is true.

Reality: A p-value is a tail probability for the specified test statistic under the null and the rest of the statistical model, including the sampling/analysis procedure. It is not a posterior probability that a hypothesis is true.

Correct interpretation: "Under this null model and analysis procedure, a test statistic at least this extreme has probability .05." Selection or unaccounted optional stopping can invalidate this calibration.

Pitfall 2: Non-Significant = No Effect

Misconception: p > .05 proves there's no effect.

Reality: Absence of evidence ≠ evidence of absence. Non-significant results may indicate:

• Insufficient statistical power
• True effect too small to detect
• High variability
• Small sample size

Better approach:

• Report confidence intervals
• Compare the interval with effects of practical importance; do not calculate power from the observed effect to explain this result
• Consider equivalence testing with scientifically justified, prespecified bounds

Pitfall 3: Significant = Important

Misconception: Statistical significance means practical importance.

Reality: With large samples, effects too small to matter for the decision can become "significant." Judge magnitude against a justified practical threshold.

Better approach:

• Report effect sizes
• Consider practical significance
• Use confidence intervals

Pitfall 4: P = .049 vs. P = .051

Misconception: These are meaningfully different because one crosses the .05 threshold.

Reality: These represent nearly identical evidence. The .05 threshold is arbitrary.

Better approach:

• Interpret p-values continuously as model-compatibility summaries, not stand-alone evidence scores
• Report exact p-values
• Consider context and prior evidence

Pitfall 5: One-Tailed Tests Without Justification

Misconception: One-tailed tests are free extra power.

Reality: A one-sided test addresses a directional hypothesis; the opposite direction need not be impossible. Choosing the tail after seeing data invalidates the nominal error rate.

When appropriate: Prespecify a directional decision and error criterion (for example, a justified non-inferiority margin). Still report estimates, uncertainty, and possible harm.

Multiple Comparisons Problems

Pitfall 6: Multiple Testing Without Correction

Problem: For 20 independent tests of true nulls at alpha .05, the probability of at least one false rejection is 1 - 0.95**20 = 0.6415 (about 64%). Dependence changes this value.

Examples:

• Testing many outcomes
• Testing many subgroups
• Conducting multiple interim analyses
• Testing at multiple time points

Solutions:

• Bonferroni correction (divide α by number of tests)
• False Discovery Rate (FDR) control
• Prespecify primary outcome
• Treat exploratory analyses as hypothesis-generating

Define the hypothesis family and error target first. FWER limits the probability of any false rejection; FDR limits the expected false-discovery proportion (zero when there are no discoveries). Neither is the probability that a particular discovery is false. A named primary outcome does not resolve multiplicity across doses, time points, interim looks, subgroups, or data-selected analysis choices.

Pitfall 7: Subgroup Analysis Fishing

Problem: Testing many subgroups until finding significance.

Why problematic:

• Inflates false positive rate
• Often reported without disclosure
• A significant result in women and a non-significant result in men does not establish a difference between groups; estimate and test the interaction directly

Solutions:

• Prespecify subgroups
• Use interaction tests, not separate tests
• Require replication
• Correct for multiple comparisons

Pitfall 8: Outcome Switching

Problem: Analyzing many outcomes, reporting only significant ones.

Detection signs:

• Secondary outcomes emphasized
• Incomplete outcome reporting
• Discrepancy between registration and publication

Solutions:

• Preregister all outcomes
• Report all planned outcomes
• Distinguish primary from secondary

Sample Size and Power Issues

Pitfall 9: Underpowered Studies

Problem: Small samples have low probability of detecting true effects.

Consequences:

• High false negative rate
• Among selected significant findings, the false-discovery fraction depends on power, prior prevalence of real effects, bias, and multiplicity; low power alone does not increase a correctly calibrated test's Type I error above its alpha
• Overestimated effect sizes (when significant)

Solutions:

• Conduct a priori power analysis
• Justify power or precision targets for the decision; 80-90% are conventions, not guarantees
• Use a meaningful effect and plausible variance; assess uncertainty in small pilot estimates

Pitfall 10: Post-Hoc Power Analysis

Problem: Calculating "observed power" using the observed effect and the same test is circular and uninformative. This does not prohibit design sensitivity calculations at an independently justified effect size.

Why useless:

• Non-significant results always have low "post-hoc power"
• It recapitulates the p-value without new information

Better approach:

• Calculate confidence intervals
• Plan replication with adequate sample
• Conduct prospective power analysis for future studies

Pitfall 11: Small Sample Fallacy

Problem: Trusting results from very small samples.

Issues:

• High sampling variability
• Outliers have large influence
• Distributional approximations may be unreliable; small n alone is not an assumption violation
• Confidence intervals very wide

Guidelines:

• There is no universal n = 30 validity threshold; count independent units and inspect precision
• Check assumptions carefully
• Choose methods for the estimand and design; non-parametric methods also have assumptions
• Replicate findings

Effect Size Misunderstandings

Pitfall 12: Ignoring Effect Size

Problem: Focusing only on significance, not magnitude.

Why problematic:

• Significance ≠ importance
• Can't compare across studies
• Doesn't inform practical decisions

Solutions:

• Always report effect sizes
• Report effects in interpretable original units or absolute risks; add standardized measures (Cohen's d, r, η²) when they answer the comparison of interest
• Interpret using field conventions
• Consider minimum clinically important difference

Pitfall 13: Misinterpreting Standardized Effect Sizes

Problem: Treating Cohen's d = 0.5 as "medium" without context.

Reality:

• Field-specific norms vary
• Some fields have larger typical effects
• Real-world importance depends on context

Better approach:

• Compare to effects in same domain
• Consider practical implications
• Look at raw effect sizes too

Pitfall 14: Confusing Explained Variance with Importance

Problem: "Only explains 5% of variance" = unimportant.

Reality:

• A small explained-variance fraction can still matter for an important outcome
• Complex phenomena have many small contributors
• Predictive accuracy ≠ causal importance

Consideration: Context matters more than percentage alone.

Correlation and Causation

Pitfall 15: Correlation Implies Causation

Problem: Inferring causation from correlation.

Alternative explanations:

• Reverse causation (B causes A, not A causes B)
• Confounding (C causes both A and B)
• Coincidence
• Selection bias

Causal appraisal: Specify the intervention/exposure contrast, population, and outcome. Assess temporality, exchangeability/confounding, positivity, consistency, selection, and measurement assumptions. Observational causal inference is possible under defensible assumptions; randomization does not repair missing outcomes or post-randomization selection.

Pitfall 16: Ecological Fallacy

Problem: Inferring individual-level relationships from group-level data.

Example: Countries with more chocolate consumption have more Nobel laureates doesn't mean eating chocolate makes you win Nobels.

Why problematic: Group-level correlations may not hold at individual level.

Pitfall 17: Simpson's Paradox

Problem: Trend appears in groups but reverses when combined (or vice versa).

Example: Treatment appears worse overall but better in every subgroup.

Cause: Different group weights can reverse marginal and conditional associations. The stratifying variable is not automatically a confounder; it may be a mediator or collider.

Solution: Choose adjustment from the causal question and temporal structure, not from whichever stratification gives the preferred answer.

Regression and Modeling Pitfalls

Pitfall 18: Overfitting

Problem: Model fits sample data well but doesn't generalize.

Causes:

• Too many predictors relative to sample size
• Fitting noise rather than signal
• No cross-validation

Solutions:

• Use cross-validation with all learned preprocessing and tuning inside training folds
• Penalized regression (LASSO, ridge)
• Independent test set
• Simpler models

Pitfall 19: Extrapolation Beyond Data Range

Problem: Predicting outside the range of observed data.

Why dangerous:

• Relationships may not hold outside observed range
• Increased uncertainty not reflected in predictions

Solution: Label extrapolation, justify transport/model assumptions, and assess sensitivity. In-range predictions can also fail under population or measurement shifts.

Pitfall 20: Ignoring Model Assumptions

Problem: Using statistical tests without checking assumptions.

Common violations:

• Incorrect distributional assumptions for the relevant errors/conditional outcomes; not all parametric models require normally distributed raw data
• Heteroscedasticity (unequal variances)
• Non-independence
• Linearity
• Rank deficiency or unstable coefficient estimation; some predictor correlation is allowed

Solutions:

• Check assumptions with diagnostics
• Use robust methods
• Transform data
• Use appropriate non-parametric alternatives

Pitfall 21: Treating Non-Significant Covariates as Eliminating Confounding

Problem: "We controlled for X and it wasn't significant, so it's not a confounder."

Reality: Non-significant covariates can still be important confounders. Significance ≠ confounding.

Solution: Prespecify an appropriate adjustment set from causal knowledge; do not select confounders by p-values or automatically adjust for mediators/colliders.

Pitfall 22: Collinearity Masking Effects

Problem: When predictors are highly correlated, true effects may appear non-significant.

Manifestations:

• Large standard errors
• Unstable coefficients
• Sign changes when adding/removing variables

Detection:

• Variance Inflation Factors (VIF)
• Correlation matrices

Solutions:

• Remove redundant predictors
• Combine correlated variables
• Use regularization methods

Regularization may stabilize prediction but does not make a non-identifiable effect identified by the data. Check design rank, parameter symmetries, profiles/sensitivity, and dependence on constraints or priors. Good fit and convergence are insufficient.

Specific Test Misuses

Pitfall 23: Uncontrolled Pairwise Comparisons

Problem: Treating many unadjusted pairwise tests as one confirmatory analysis.

Correct approach: Prespecify contrasts and an appropriate familywise or other error strategy. An omnibus ANOVA is useful for its own question but is not a universal prerequisite for planned contrasts, and a significant omnibus test does not authorize all unadjusted pairs.

Pitfall 24: Pearson Correlation for Non-Linear Relationships

Problem: Using Pearson's r for curved relationships.

Why misleading: r measures linear relationships only.

Solutions:

• Check scatterplots first
• Use Spearman's ρ for monotonic relationships
• Consider polynomial or non-linear models

Pitfall 25: Chi-Square with Small Expected Frequencies

Problem: Relying on an asymptotic chi-square approximation with sparse expected counts. The often-used count-of-five rule is a heuristic, not a universal validity boundary.

Solutions:

• Fisher's exact test
• Combine categories only for a prespecified substantive reason, not to obtain significance
• Increase sample size

Pitfall 26: Paired vs. Independent Tests

Problem: Using independent samples test for paired data (or vice versa).

Why wrong:

• Ignoring real dependence can misestimate uncertainty in either direction
• Inventing pairs changes the estimand and may discard data or distort uncertainty

Solution: Match test to design.

Confidence Interval Misinterpretations

Pitfall 27: 95% CI = 95% Probability True Value Inside

Misconception: "95% chance the true value is in this interval."

Reality: For a correctly calibrated frequentist 95% interval procedure under its assumptions, 95% of intervals across repetitions cover the fixed parameter. An individual interval does not assign a 95% posterior probability to that parameter.

Better reporting: Give the estimate, interval, confidence level, assumptions, and whether the interval excludes effects important to the scientific decision.

Pitfall 28: Overlapping CIs = No Difference

Problem: Assuming overlapping confidence intervals mean no significant difference.

Reality: Overlapping CIs are less stringent than difference tests. Two CIs can overlap while the difference between groups is significant.

Guideline: Estimate the contrast and its interval directly, accounting for covariance. Neither overlap heuristic substitutes for that calculation.

Pitfall 29: Ignoring CI Width

Problem: Focusing only on whether CI includes zero, not precision.

Why important: Wide CIs indicate high uncertainty. "Significant" effects with huge CIs are less convincing.

Consider: Both significance and precision.

Bayesian vs. Frequentist Confusions

Pitfall 30: Mixing Bayesian and Frequentist Interpretations

Problem: Making Bayesian statements from frequentist analyses.

Examples:

• "Probability hypothesis is true" (Bayesian) from p-value (frequentist)
• "Evidence for no meaningful effect" from a non-significant test alone; frequentist equivalence tests can address prespecified bounds, not prove an exact point null

Solution:

• Be clear about framework
• Use Bayesian methods for Bayesian questions
• For Bayes factors, specify competing models and priors and examine prior sensitivity

Pitfall 31: Ignoring Prior Probability

Problem: Treating all hypotheses as equally likely initially.

Reality: Extraordinary claims need extraordinary evidence. Prior plausibility matters.

Consider:

• Plausibility given existing knowledge
• Mechanism plausibility
• Base rates

Data Transformation Issues

Pitfall 32: Dichotomizing Continuous Variables

Problem: Splitting continuous variables at arbitrary cutoffs.

Consequences:

• Loss of information and power
• Arbitrary distinctions
• Discarding individual differences

Exceptions: Clinically meaningful cutoffs with strong justification.

Better: Model the continuous relationship, including nonlinear terms when justified; adding arbitrary categories still loses information.

Pitfall 33: Trying Multiple Transformations

Problem: Testing many transformations until finding significance.

Why problematic: Inflates Type I error, is a form of p-hacking.

Better approach:

• Prespecify transformations
• Use theory-driven transformations
• Correct for multiple testing if exploring

Missing Data Problems

Pitfall 34: Listwise Deletion by Default

Problem: Automatically deleting all cases with any missing data.

Consequences:

• Reduced power
• Potential bias if data not missing completely at random (MCAR)

Better approaches:

• Multiple imputation
• Maximum likelihood methods
• Analyze missingness patterns

Pitfall 35: Ignoring Missing Data Mechanisms

Problem: Not considering why data are missing.

Types:

• MCAR: missingness independent of observed and unobserved data; deletion can lose precision
• MAR: conditional on the observed variables used, missingness is independent of missing values; imputation/likelihood methods still require correctly specified, compatible models
• MNAR: residual dependence on missing values; examine plausible sensitivity scenarios

Solution: Record reasons, timing, and assumptions. Observed missingness patterns cannot establish MAR versus MNAR. Pool imputation uncertainty; single mean imputation is not a fix.

Publication and Reporting Issues

Pitfall 36: Selective Reporting

Problem: Only reporting significant results or favorable analyses.

Consequences:

• Literature appears more consistent than reality
• Meta-analyses biased
• Wasted research effort

Solutions:

• Preregistration
• Report all analyses
• Use reporting guidelines (CONSORT, PRISMA, etc.)

Pitfall 37: Rounding to p < .05

Problem: Reporting exact p-values selectively (e.g., p = .049 but p < .05 for .051).

Why problematic: Obscures values near threshold, enables p-hacking detection evasion.

Better: Always report exact p-values.

Pitfall 38: No Data Sharing

Problem: Not making data available for verification or reanalysis.

Consequences:

• Can't verify results
• Some independent checks or individual-participant-data analyses may be impossible; published aggregate estimates can still support an appropriate meta-analysis
• Hinders scientific progress

Best practice: Share data unless privacy concerns prohibit.

Cross-Validation and Generalization

Pitfall 39: No Cross-Validation

Problem: Testing model on same data used to build it.

Consequence: Overly optimistic performance estimates.

Solutions:

• Split data (train/test)
• K-fold cross-validation
• Independent validation sample

Pitfall 40: Data Leakage

Problem: Information from test set leaking into training.

Examples:

• Normalizing before splitting
• Feature selection on full dataset
• Including temporal information

Consequence: Inflated performance metrics.

Prevention: Fit learned preprocessing only on the training portion of each fold; tune within that boundary and reserve an untouched evaluation set. Split by independent subject, site, batch, or time as the deployment question requires; technical replicates must not leak.

Meta-Analysis Pitfalls

Pitfall 41: Apples and Oranges

Problem: Combining studies with different designs, populations, or measures.

Balance: Need homogeneity but also comprehensiveness.

Solutions:

• Clear inclusion criteria
• Subgroup analyses
• Meta-regression for moderators

Pitfall 42: Ignoring Publication Bias

Problem: Published studies overrepresent significant results.

Consequences: Overestimated effects in meta-analyses.

Assessment: Compare protocols/registries and reported outcomes; seek eligible unpublished results. Funnel asymmetry indicates small-study effects, not necessarily publication bias. Asymmetry tests generally need at least ten studies with varying precision and a method appropriate to the effect measure; a negative test cannot exclude missing evidence.

Sensitivity analysis: Trim-and-fill, selection models, PET-PEESE, and p-curve have different assumptions and targets. Do not describe adjusted estimates as recovered truth or treat fail-safe N as a reliability certificate.

Pitfall 43: Pseudoreplication and Changing Denominators

Repeated measurements, cells from one donor, or wells from one culture are not automatically independent biological replicates. Identify assignment and sampling units; use an appropriate hierarchical/repeated-measures analysis or justified aggregation. Report independent-unit n separately from measurement count. A mean of group percentages differs from the pooled numerator/denominator when group sizes differ; state weighting, evaluable counts, and exclusions.

General Best Practices

1. Preregister studies - Distinguish confirmatory from exploratory
2. Report transparently - All analyses, not just significant ones
3. Check assumptions - Don't blindly apply tests
4. Use appropriate tests - Match test to data and design
5. Report effect sizes - Not just p-values
6. Consider practical significance - Not just statistical
7. Replicate findings - One study is rarely definitive
8. Share data and code - Enable verification
9. Use confidence intervals - Show uncertainty
10. Think causally carefully - Most research is correlational