NZ Scholarship Statistics cheat sheet

Experimental design: random allocation balances unmeasured confounders in expectation; blocking reduces variance by grouping similar units; pairing is blocking with block size two.

Observational vs experimental: only random assignment supports causal claims; random sampling supports generalisation to a population. These are separate concerns.

Bias types to name precisely: selection, response/non-response, recall, measurement, survivorship, and confounding - each has a distinct remedy.

Sampling distributions: SE of a mean is sigma/sqrt(n); SE of a proportion is sqrt(p(1-p)/n). Quadrupling n halves the standard error.

Central limit theorem: sample means are approximately normal for large n regardless of population shape; normality arrives faster for symmetric populations.

Confidence interval logic: a 95% interval is a procedure that captures the parameter in 95% of repeated samples - not a 95% probability for a fixed parameter.

Margin of error is roughly 2 SE for 95% confidence; it shrinks with sqrt(n), so to halve it you need four times the sample size.

Formal inference: t procedures when sigma is estimated and the sample is small; z procedures when sigma is known or n is large. Check independence and skew first.

Hypothesis test structure: state H0 and HA in terms of parameters, compute a test statistic, convert to a p-value, then interpret in context without claiming P(H0 true).

A p-value is the probability of data at least as extreme as observed, assuming H0; it is not the probability the null is true nor the probability of a mistake.

Type I error: rejecting a true H0, probability alpha. Type II error: failing to reject a false H0, probability beta. Power is 1 - beta and rises with effect size, n, and lower alpha.

Two-sided vs one-sided tests: choose before seeing data; a one-sided test halves the p-value only if the effect is in the predicted direction.

Statistical significance is not practical significance: with very large n, trivial effects become significant; report effect size and interval width alongside p.

Multiple comparisons inflate familywise error; Bonferroni divides alpha by the number of tests, preserving familywise control at the cost of power.

Chi-square goodness of fit compares observed to expected counts; expected counts below about five make the chi-square approximation unreliable.

Correlation and regression: r measures linear association only, is unaffected by rescaling, and is sensitive to outliers; regression predicts y from x, not the reverse.

Conditional probability: P(A|B) = P(A and B)/P(B). Independence means P(A|B) = P(A), equivalently P(A and B) = P(A)P(B).

Bayes' theorem: P(A|B) = P(B|A)P(A) / P(B), with P(B) expanded by the law of total probability over a partition of the sample space.

Base-rate neglect: a highly accurate test for a rare condition still yields mostly false positives when prevalence is very low; compute posterior, not intuition.

Discrete expectation: E(X) = sum x P(x); variance is E(X^2) - [E(X)]^2. For linear combinations, E(aX + bY) = aE(X) + bE(Y) always.

Var(aX + bY) = a^2 Var(X) + b^2 Var(Y) + 2ab Cov(X,Y); the covariance term vanishes under independence.

Binomial conditions: fixed n, independent trials, constant p, two outcomes. Mean np, variance np(1-p). The Poisson approximates it for large n and small p.

Geometric distribution: number of trials until first success, mean 1/p; memoryless, so past failures do not change future probabilities.

Normal calculations: standardise with z = (x - mu)/sigma, then use symmetry and tables; the empirical rule gives 68%, 95%, 99.7% within 1, 2, 3 sigma.

Report answers in context: name the variable, units, direction of effect, and uncertainty; a bare number without interpretation loses communication marks.

Justify method choice explicitly: state assumptions (independence, normality, random sampling) and what happens if they fail, rather than asserting a test is valid.

Show algebra symbolically before substituting numbers; setting up the correct expression earns credit even if arithmetic slips.

When comparing groups, report both a difference and an interval for that difference; non-overlapping intervals imply a significant difference, overlapping ones do not imply the reverse.

Simulation reasoning: a randomisation test shuffles group labels to build the null distribution; a bootstrap resamples with replacement to estimate sampling variability.

Recognise when a question asks for prediction versus inference: prediction intervals are wider than confidence intervals because they add residual variance.

Sensitivity check: recompute after removing an influential point or changing an assumption; if conclusions flip, the finding is fragile and should be reported as such.

Guard against ecological and Simpson's paradox reasoning: aggregated trends can reverse when data are split by a lurking grouping variable.

Question the source of data: who collected it, when, on whom, and whether the sample was self-selected; volunteer samples cannot support population estimates.

Check the denominator: counts without a base rate are uninterpretable; a doubling from 1 to 2 cases is not the same as a doubling from 10,000 to 20,000.

Graphical integrity: truncated axes exaggerate differences, area or volume encodings distort perception, and 3-D effects mislead; check axis start and scale.

Beware of absolute versus relative risk framing: a 50% relative reduction of a tiny baseline risk may be a negligible absolute change.

Confounding versus mediation: a confounder distorts the exposure-outcome relation; a mediator lies on the causal pathway and should not be adjusted away casually.

Regression to the mean: extreme measurements tend to be followed by less extreme ones without any intervention; naive before-after comparisons overstate effects.

Publication and reporting bias: significant results are more likely to be published and reported, so meta-analytic summaries can overstate effect sizes.

Causal language requires design support: words like 'causes' or 'leads to' need randomisation or strong quasi-experimental identification, not just correlation.

Five-number summary: minimum, lower quartile, median, upper quartile, maximum. The IQR is Q3 - Q1; the 1.5 IQR rule flags outliers beyond Q1 - 1.5 IQR or Q3 + 1.5 IQR.

Shape diagnostics: compare mean and median; mean greater than median suggests right skew, and the reverse suggests left skew.

Standard deviation is in the units of the data and is pulled upward by outliers; IQR is resistant and preferred for skewed data.

Transformations: logarithms linearise multiplicative relationships and reduce right skew; a square root suits moderate counts, and the reciprocal suits rates.

Scatterplot reading: describe form, direction, strength, and outliers before quoting r; a curved pattern makes r misleading even if it is large.

Residual plots diagnose regression fit: curvature suggests a missing term, fanning suggests heteroscedasticity, and patternless scatter supports the linear model.

Simpson's paradox: an association can reverse direction when data are aggregated across groups; always check within-group relationships.

Two-way tables: compare conditional distributions (row percentages) rather than joint counts, and look for the interaction before summarising marginals.

Completely randomised design: treatments assigned at random to all units. Randomised block design: units grouped by a blocking variable, then randomised within blocks.

Matched pairs design: each unit receives both treatments in random order, or paired units are matched on a covariate before random allocation.

Replication versus repetition: replication means independent experimental units per treatment; repeated measures on one unit do not increase the effective sample size.

Blinding: single-blind hides treatment from the subject, double-blind also from the assessor; both reduce placebo and measurement bias.

Control group purpose: provides a baseline for comparison; without it, change over time cannot be separated from treatment effect.

Factorial designs estimate main effects and interactions; an interaction means the effect of one factor depends on the level of another, so main effects alone mislead.

Sample size planning: power depends on effect size, variability, alpha, and n; specify a minimum detectable effect before collecting data.

Ethical and practical constraints: randomisation requires informed consent and equipoise; when unavailable, use natural experiments or matching, and state the limitation.

Time series components: trend, seasonal, cyclical, and irregular. Additive decomposition suits constant seasonal amplitude; multiplicative suits amplitude growing with level.

Smoothing: moving averages of period k remove a seasonal pattern of length k; a centred moving average is needed for even k to align with time points.

Seasonal indices: average the detrended values for each season, then adjust so indices sum to the number of seasons (or mean 1) before forecasting.

Autocorrelation measures correlation between a series and its lagged self; slowly decaying autocorrelation indicates trend or non-stationarity.

Least-squares line: slope b = r(sy/sx), intercept a = ybar - b xbar; the line passes through the point of means.

Coefficient of determination r^2 is the proportion of variation in y explained by the linear regression on x; it does not establish causation.

Extrapolation risk: a fitted trend is unreliable outside the observed x-range, especially when the underlying relationship is nonlinear or regime-shifting.

Forecast comparison: report error measures such as mean absolute error or root mean squared error on held-out data, not on the fitting data.