{
  "id": "power-analysis",
  "title": "Power Analysis",
  "lang": "en",
  "source_lang": "en",
  "summary": "Power analysis quantifies a statistical procedure’s probability of detecting specified effects and supports the design, sizing, and evaluation of studies.",
  "category": "mathematics",
  "subcategory": "probability-statistics",
  "type": "concept",
  "aliases": [
    "Statistical power analysis"
  ],
  "generated_at": "2026-11-04",
  "model": "pro/gpt-6.1-sol",
  "url": "https://aiwiki.page/en/power-analysis/",
  "translations": {
    "zh-Hans": {
      "url": "https://aiwiki.page/zh/power-analysis/",
      "json": "https://aiwiki.page/zh/power-analysis.json"
    }
  },
  "sections": [
    {
      "heading": "",
      "text": "Power analysis is the study of how likely a statistical test is to reject a specified null hypothesis when a particular alternative is true. It connects statistical power with the size of an effect, the amount and quality of information collected, and the rules used to analyze the data. Its most familiar application is determining the sample size needed for a planned experiment, but it also supports comparisons among designs, assessments of detectable effects, and evaluations of uncertainty about a study’s operating characteristics.\n\nA power calculation is conditional on assumptions. A statement that a study has 80% power is incomplete unless it identifies the effect being considered, the statistical procedure, the significance threshold, and relevant assumptions about variability, dependence, and data loss. Power is not the probability that a hypothesis is true, nor is it a guarantee that a particular study will produce a statistically significant result.\n\nThe subject belongs to statistics and experimental design, with applications ranging from laboratory experiments and industrial testing to surveys, education research, and randomized trials. Its methods include exact probability calculations, large-sample approximations, numerical integration, and simulation. More elaborate analyses incorporate multiple outcomes, clustered observations, sequential decisions, and uncertainty about the quantities used in planning."
    },
    {
      "heading": "Statistical foundations and historical development",
      "text": "In statistical hypothesis testing, a decision rule divides possible datasets into those that lead to rejection of a null hypothesis and those that do not. If \\(X\\) denotes the data, \\(\\theta\\) a parameter, and \\(\\mathcal R\\) the rejection region, the power function is\n\n\\[\\pi(\\theta)=\\Pr_\\theta(X\\in\\mathcal R).\\]\n\nFor parameter values belonging to the alternative hypothesis, this is the probability of detecting a departure from the null in the particular sense defined by the test. The probability of failing to reject at such a value is conventionally denoted \\(\\beta(\\theta)\\), so power equals \\(1-\\beta(\\theta)\\). Power is therefore generally a function, not a single property that a study possesses independently of the true parameter.\n\nThe significance level, usually denoted \\(\\alpha\\), constrains false rejection under the null. For a composite null parameter space \\(\\Theta_0\\), a level-\\(\\alpha\\) test satisfies\n\n\\[\\sup_{\\theta\\in\\Theta_0}\\Pr_\\theta(X\\in\\mathcal R)\\leq\\alpha.\\]\n\nThis distinguishes the two principal types of testing error: rejecting a true null and failing to reject a false one. For a fixed sample size and model, making false rejection less likely will ordinarily reduce power against a given alternative. The trade-off cannot be assessed without specifying both the decision rule and the alternative of interest.\n\nThe modern framework developed substantially through Jerzy Neyman and Egon Pearson’s work, particularly their 1933 paper on the most efficient tests of statistical hypotheses. Their approach treated tests as procedures whose repeated-sampling error probabilities could be compared. For testing a simple null against a simple alternative, the Neyman–Pearson lemma establishes the optimality of a likelihood-ratio rejection rule under a fixed Type I error constraint. This theoretical setting differs in emphasis from Ronald Fisher’s significance-testing approach, although elements of both traditions are often combined in applied practice.\n\nJacob Cohen helped make power analysis a routine concern in behavioral research. His 1962 examination of research published in the Journal of Abnormal and Social Psychology emphasized the limited power of many studies for effects of plausible magnitude. His book Statistical Power Analysis for the Behavioral Sciences, first published in 1969 and issued in a second edition in 1988, supplied accessible conventions and calculation methods.\n\nValues such as 80% or 90% power subsequently became common planning targets. They are conventions, not mathematical requirements. An appropriate operating characteristic depends on the scientific question, the consequences of each kind of error, feasibility, and the other purposes of the study. Moreover, power to reject a hypothesis and precision in estimating a parameter are related but distinct design criteria."
    },
    {
      "heading": "Analytical calculations and the sample-size relationship",
      "text": "The simplest calculations concern a normally distributed outcome with known variability. Suppose \\(X_1,\\ldots,X_n\\) are independent observations with mean \\(\\mu\\) and known standard deviation \\(\\sigma\\). To test \\(H_0:\\mu=\\mu_0\\), the standardized sample mean is\n\n\\[Z=\\frac{\\bar X-\\mu_0}{\\sigma/\\sqrt n}.\\]\n\nUnder the null, \\(Z\\) follows the standard normal distribution. Under a true difference \\(\\Delta=\\mu-\\mu_0\\), its mean is shifted by \\(\\lambda=\\Delta\\sqrt n/\\sigma\\), while its variance remains one. This shift expresses the basic signal-to-noise relationship underlying many power calculations.\n\nFor a two-sided test, let \\(c=z_{1-\\alpha/2}\\), where \\(z_q\\) is the standard normal quantile at probability \\(q\\). If \\(\\Phi\\) denotes the standard normal cumulative distribution function, power is\n\n\\[\\pi(\\Delta)=1-\\Phi(c-\\lambda)+\\Phi(-c-\\lambda).\\]\n\nPower increases as the magnitude of the shift grows. Increasing the effect or decreasing measurement variability moves the alternative distribution farther from the rejection boundaries. Increasing sample size has the same effect, but only through \\(\\sqrt n\\): doubling the standardized separation requires approximately four times as many observations.\n\nFor two independent groups of equal size \\(n\\), with a common known standard deviation, the standard error of the difference in means is \\(\\sigma\\sqrt{2/n}\\). A widely used normal approximation gives the required number per group as\n\n\\[n\\approx \\frac{2\\sigma^2\\left(z_{1-\\alpha/2}+z_{1-\\beta}\\right)^2}{\\Delta^2}.\\]\n\nThe expression neglects the usually small rejection probability in the tail opposite to the assumed effect. With a standardized difference \\(d=\\Delta/\\sigma=0.5\\), two-sided \\(\\alpha=0.05\\), and target power \\(0.80\\), it gives approximately 63 participants per group. An exact calculation for the equal-variance two-sample \\(t\\)-test requires about 64 per group.\n\nUnknown variance changes the calculation. A \\(t\\)-test uses Student’s t-distribution under the null and a noncentral distribution under an alternative. Both the noncentrality parameter and the degrees of freedom depend on sample size, so numerical root-finding is commonly used to determine the smallest integer sample meeting the power target.\n\nThe familiar inverse-square relationship also explains why detecting small effects can be expensive. Halving the target difference approximately quadruples the sample requirement when other assumptions remain fixed. This relationship is not universal: rare events, discrete tests, small numbers of clusters, and adaptive procedures can produce substantial departures from the simple approximation."
    },
    {
      "heading": "Effect specification and scientifically meaningful alternatives",
      "text": "The effect size used in planning determines what a power calculation actually promises. For a difference in means, an effect can be expressed in the outcome’s original units or divided by a standard deviation. For binary outcomes, it might be a risk difference, risk ratio, or odds ratio. For a regression model, it may be a coefficient or a specified improvement in model fit. These quantities are not interchangeable, even when they describe the same underlying comparison.\n\nOriginal measurement units often make the research question most explicit. A difference of five units on an instrument has a substantive interpretation only through that instrument’s scale and the context of measurement. A standardized difference additionally depends on the population’s variability. Thus, the same physical or behavioral difference can produce different standardized effects in homogeneous and heterogeneous populations. Generic labels such as “small,” “medium,” and “large” do not establish scientific importance.\n\nAn effect for planning may come from prior studies, a scientifically important threshold, a mechanistic model, or a range of plausible alternatives. These sources answer different questions. Power at the smallest effect considered important addresses whether the study can reliably detect that threshold under its assumptions. Power at a best estimate of the expected effect addresses performance under a particular forecast. Substituting a convenient conventional effect size for either quantity changes the interpretation of the design.\n\nPilot studies are often more informative about recruitment, measurement procedures, and feasibility than about the true effect. Their effect estimates can be highly variable. If a pilot happens to overestimate the signal or underestimate the variance, using its estimates without allowance for uncertainty can yield an inadequate main study. Estimates selected because an earlier result was significant can be especially optimistic, a problem connected to publication bias and selective reporting.\n\nThe alternative must also match the hypothesis. In equivalence testing, the aim is to establish that a parameter lies within prespecified bounds, rather than merely fail to reject equality. A common procedure performs two one-sided tests. At one-sided level \\(0.05\\), this corresponds to requiring a 90% confidence interval to lie entirely inside the equivalence bounds. Power depends on the true effect’s location relative to both bounds.\n\nNoninferiority testing instead evaluates whether a disadvantage is smaller than a specified margin. A design powered for superiority cannot be assumed to have adequate noninferiority power, or vice versa. In each case, the margin, direction of comparison, and assumed true effect are separate inputs. A small p-value against equality does not itself establish that an effect exceeds a scientifically important threshold."
    },
    {
      "heading": "Outcomes, statistical models, and information",
      "text": "Different outcomes carry information in different ways. For two independent binary outcomes with event probabilities \\(p_1\\) and \\(p_2\\), the variance of the observed difference in proportions is\n\n\\[\\operatorname{Var}(\\hat p_1-\\hat p_2) = \\frac{p_1(1-p_1)}{n_1} + \\frac{p_2(1-p_2)}{n_2}.\\]\n\nConsequently, specifying only a risk difference is insufficient: the baseline probability is also needed. A difference between 0.05 and 0.10 has different variability from a difference between 0.45 and 0.50. Calculations for binary data may use normal approximations, exact enumeration under a binomial distribution, or simulation of the intended model and test.\n\nCount outcomes introduce analogous dependencies. Under a Poisson distribution, the variance equals the mean, so power depends on the event rate and exposure as well as the rate ratio. If actual variability exceeds the Poisson assumption, a calculation that ignores this overdispersion can overstate power. Zeros, unequal follow-up, and dependence between repeated counts may also alter the relevant sampling model.\n\nFor linear regression, power to test a coefficient depends on residual variability and on how much independent information its predictor contributes. A predictor that is strongly related to other predictors can have a large coefficient standard error even in a sizable dataset. In a fixed-design model with independent, equal-variance errors,\n\n\\[\\operatorname{Var}(\\hat{\\boldsymbol\\beta}) = \\sigma^2(X^\\mathsf{T}X)^{-1}.\\]\n\nThe matrix \\(X^\\mathsf{T}X\\) therefore links design geometry to precision and power. Rules based only on a number of observations per predictor do not capture the strength of predictor relationships, the targeted contrast, or the residual variance.\n\nTests in analysis of variance commonly use noncentral \\(F\\)-distributions. An omnibus test asks whether a set of means or coefficients differs somewhere; it need not have the same power as a particular planned comparison. Likewise, power for a statistical interaction concerns a difference between effects, not either effect separately. A significant result in one subgroup and a nonsignificant result in another is not itself evidence of an interaction.\n\nIn survival analysis, the number and timing of observed events are often more directly relevant than the number enrolled. Under proportional hazards and a standard log-rank approximation, the required event count is approximately\n\n\\[D\\approx \\frac{\\left(z_{1-\\alpha/2}+z_{1-\\beta}\\right)^2} {q(1-q)\\left(\\log HR\\right)^2},\\]\n\nwhere \\(q\\) is the allocation fraction and \\(HR\\) the assumed hazard ratio. Translating events into enrollment requires assumptions about recruitment, follow-up, censoring, and event incidence. When hazards are not proportional, a single hazard ratio may poorly characterize both the effect and the power of the chosen test."
    },
    {
      "heading": "Dependence, allocation, and the structure of a design",
      "text": "Observations contribute less independent information when their outcomes are correlated. In a simple cluster-randomized design with equal cluster size \\(m\\) and intracluster correlation \\(\\rho\\), the conventional design effect is\n\n\\[\\mathrm{DE}=1+(m-1)\\rho.\\]\n\nMultiplying an individually randomized sample-size requirement by this factor gives a rough adjustment for clustering. For example, clusters of 30 observations with \\(\\rho=0.05\\) have a design effect of \\(2.45\\). A nominal total of 600 observations then has an approximate effective sample size of \\(600/2.45\\), or 245, under this simplified variance comparison.\n\nThe formula does not fully characterize cluster trials. Unequal cluster sizes, different outcome models, covariate adjustment, and small numbers of clusters require additional treatment. Because randomization occurs at the cluster level, the number of clusters strongly affects the available degrees of freedom and the reliability of variance estimates. Adding more individuals to a few existing clusters may yield much less information than adding new clusters, particularly when within-cluster similarity is substantial.\n\nPairing can improve power rather than reduce it. For paired observations with equal marginal variance \\(\\sigma^2\\) and within-pair correlation \\(r\\), the variance of their difference is\n\n\\[\\operatorname{Var}(X_1-X_2)=2\\sigma^2(1-r).\\]\n\nPositive correlation reduces the variability of the contrast. A paired or crossover design may therefore require fewer participants than an independent-groups design for the same target difference. Its power calculation must nevertheless reflect the actual analysis, including period effects, incomplete pairs, and any relevant carryover structure.\n\nRepeated measurements can similarly increase precision, but their value depends on the covariance matrix across occasions. Ten highly correlated observations from one participant are not equivalent to ten independent participants. Longitudinal power calculations may need to distinguish tests of an average group difference, a time trend, and a group-by-time interaction. Different assumptions about when measurements occur and how correlations decay can materially change the result.\n\nAllocation also matters. With equal group variances and equal per-observation costs, balanced allocation minimizes the variance of a two-group mean difference for a fixed total sample. With unequal standard deviations \\(\\sigma_1,\\sigma_2\\) and costs \\(c_1,c_2\\), the variance-minimizing allocation under a simple fixed budget satisfies\n\n\\[\\frac{n_1}{n_2} = \\frac{\\sigma_1}{\\sigma_2}\\sqrt{\\frac{c_2}{c_1}}.\\]\n\nExpected data loss is another design component. If an analyzable sample of \\(N\\) is required and a fraction \\(r\\) is expected to be lost, the elementary enrollment inflation is \\(N/(1-r)\\). This compensates only for the assumed loss of information. It does not remove bias from informative dropout or establish the validity of a missing-data model."
    },
    {
      "heading": "Multiple hypotheses and sequential decisions",
      "text": "A study with several outcomes or comparisons has more than one possible definition of success. Marginal power is the rejection probability for one particular hypothesis. Disjunctive power is the probability of rejecting at least one false null, whereas conjunctive power is the probability of rejecting all designated false nulls. These can differ greatly, even when every individual test has the same marginal power.\n\nProcedures for multiple testing alter rejection thresholds and therefore affect sample requirements. Under the Bonferroni correction, \\(m\\) tests may each be conducted at level \\(\\alpha/m\\) to control the family-wise error probability. For ten comparisons and family-wise \\(\\alpha=0.05\\), each two-sided test uses level \\(0.005\\). The resulting critical value is larger than for an isolated test at 0.05, reducing power for the same sample and effect.\n\nDependence among test statistics can be used by less conservative procedures, but the corresponding power analysis must include their joint behavior. Hierarchical testing rules make later decisions conditional on earlier rejections, so power for a downstream claim depends on the whole testing pathway. Procedures controlling the false discovery rate introduce a different objective: their thresholds depend on the collection of observed results and, often, on the proportion and strength of true signals.\n\nRepeated examination of accumulating data creates another multiplicity problem. Applying an ordinary fixed-sample threshold at every interim analysis generally increases the probability of an eventual false rejection. Sequential analysis instead specifies boundaries or error-spending rules that account for the timing and number of looks. Power must then be computed for the complete monitoring procedure, including early stopping for benefit or futility.\n\nFor a sequential design, expected sample size and maximum sample size are distinct. Strong effects may lead to early stopping and a small expected sample size, even when the maximum planned sample exceeds that of a comparable fixed-sample design. Futility rules can reduce resources spent on weak effects, but can also lower power if they terminate some trajectories that would later have crossed the efficacy boundary.\n\nAdaptive sample-size changes require the same procedural perspective. Re-estimating a nuisance quantity such as pooled variance can behave differently from increasing enrollment after examining an unblinded treatment difference. The statistical validity and power of either approach depend on its specific adaptation rule, analysis method, and stopping conditions. Power assessed as if the final sample size had been fixed in advance may not describe the actual design. Conditional power—the probability of eventual success given interim data and an assumed future effect—is useful for describing such procedures, but is sensitive to that future-effect assumption."
    },
    {
      "heading": "Simulation-based power analysis",
      "text": "Analytical formulas become difficult when designs include complex dependence, nonlinear models, irregular follow-up, or elaborate decision rules. Simulation-based power analysis addresses this by repeatedly generating datasets under a specified alternative, analyzing each dataset with the intended procedure, and recording whether the success criterion is met. If \\(R\\) of \\(B\\) simulated datasets produce rejection, the estimated power is\n\n\\[\\hat\\pi=\\frac{R}{B}.\\]\n\nThis is an application of the Monte Carlo method. Its value lies not merely in generating artificial data, but in reproducing the full design and analysis closely enough that the resulting rejection frequency answers the intended planning question.\n\nA simulation begins with a data-generating model. This may specify participant characteristics, treatment assignment, cluster effects, outcome distributions, missingness, and recruitment. The analysis stage then implements the planned model, test, contrasts, multiplicity adjustment, and stopping rule. For a generalized linear model or mixed model, power can depend on details such as the variance estimator, degrees-of-freedom approximation, and treatment of boundary estimates.\n\nThe simulation estimate has its own uncertainty. If replications are independent, its approximate Monte Carlo standard error is\n\n\\[\\operatorname{SE}(\\hat\\pi) \\approx \\sqrt{\\frac{\\hat\\pi(1-\\hat\\pi)}{B}}.\\]\n\nAt estimated power 0.80 and \\(B=10{,}000\\), this is about 0.004, giving an approximate 95% Monte Carlo interval extending about 0.008 on either side. Such an interval describes simulation error conditional on the assumed model. It does not measure uncertainty about whether the model accurately represents the eventual study.\n\nSoftware failures are part of the operating characteristics. A fitting algorithm may fail to converge, yield an undefined standard error, or estimate a variance component at a boundary. Simply deleting unsuccessful replications estimates power conditional on successful analysis, which can be misleading. A transparent simulation distinguishes rejection, nonrejection, and computational failure, and specifies how failures affect the primary estimate.\n\nValidation commonly includes simulating under the null to check Type I error, comparing simple special cases with known formulas, and verifying the generated distributions and correlations. A procedure with a rejection probability above the intended level may appear powerful partly because it rejects too readily. Power comparisons are most informative when competing methods have appropriately controlled error rates.\n\nSimulation also permits structured sensitivity analysis. Rather than evaluating one sample size under one parameter set, an analysis can vary effect sizes, event rates, variance components, and missing-data mechanisms across a grid. The output may be a family of power curves or a table of required sample sizes. This exposes which assumptions drive the design and where an apparently adequate study becomes unreliable."
    },
    {
      "heading": "Parameter uncertainty, assurance, and alternative design criteria",
      "text": "Conventional power treats the planning inputs as fixed, although the effect, variance, event rate, or intracluster correlation is usually uncertain. A single calculation can therefore convey more certainty than the available evidence warrants. One response is to display power across plausible parameter values. Another is to average the conditional success probability over a distribution representing uncertainty about those parameters.\n\nThis second approach is often called assurance or predictive probability of study success. If \\(p(\\theta)\\) is a design distribution for the unknown parameters, assurance can be written as\n\n\\[A(n)=\\int \\Pr_\\theta(\\text{study success}\\mid n)\\, p(\\theta)\\,d\\theta.\\]\n\nThe success criterion may still be an ordinary frequentist test. Alternatively, it may require a posterior probability or another Bayesian decision threshold. The distribution used to plan the study and the inferential method used to analyze it are therefore separate features of the design.\n\nIn Bayesian inference, a prior distribution can represent uncertainty about plausible effects and nuisance parameters before data collection. If appreciable prior probability lies near no effect, assurance for a superiority claim can be substantially lower than power calculated at a favorable single effect. Averaging over uncertainty is not equivalent to calculating power at the average effect, because power is generally nonlinear in its inputs.\n\nAssurance itself depends on the chosen design distribution. Different interpretations of prior evidence can produce different values, and a precise numerical result does not eliminate that dependence. It is also distinct from the probability that the scientific hypothesis is true after observing the study, which concerns a posterior distribution rather than a pre-data success frequency.\n\nPower need not be the sole design objective. An estimation-focused study may instead require that a confidence interval attain a specified width. For a normally distributed mean with known \\(\\sigma\\), an interval half-width \\(h\\) requires approximately\n\n\\[n=\\left(\\frac{z_{1-\\alpha/2}\\sigma}{h}\\right)^2.\\]\n\nUnlike a superiority power calculation, this criterion does not require choosing a nonzero effect. Precision-based and power-based designs can nevertheless yield different sample sizes because they answer different questions.\n\nA broader decision-theoretic approach attaches consequences or utilities to outcomes and chooses a design by expected performance, cost, or expected value of information. It can account for the fact that an additional observation has a cost while better decisions have value. These approaches require explicit assumptions about consequences and uncertainty; they do not turn conventional targets such as 80% power into universal optima. They also distinguish statistical efficiency from identification: a large sample cannot by itself resolve confounding or establish a causal effect that the design does not identify."
    },
    {
      "heading": "Interpretation, retrospective calculations, and reporting",
      "text": "Prospective power is a repeated-sampling property under specified assumptions, not a forecast that an individual study will certainly succeed or fail. A procedure with 80% power will fail to reject in about 20% of repeated studies generated under the stated alternative. If the true effect is smaller than assumed, actual power will generally be lower. If the outcome variability or dependence structure differs, it may change in either direction.\n\nAfter observing data, researchers sometimes calculate “observed power” by substituting the estimated effect into the original power formula. For many common tests, this quantity is a monotonic transformation of the observed test statistic or \\(p\\)-value. It therefore supplies little or no independent evidence about the result. A nonsignificant outcome will generally produce low observed power, but that does not establish that the original design was inadequate for its prespecified effect.\n\nRetrospective calculations can still answer meaningful questions when they use an externally justified effect rather than treating the observed estimate as the truth. For example, power at a fixed important effect can be recalculated using the achieved sample size and clearly stated variance assumptions. A minimum detectable effect can likewise describe design sensitivity. Neither calculation determines whether that effect exists or substitutes for examining the estimated effect and its uncertainty.\n\nLow power also interacts with selection. When noisy estimates become visible mainly after crossing a significance threshold, the reported magnitudes can be exaggerated. Across replications, studies may then disagree in statistical significance even when their estimates are compatible within sampling error. Power is relevant to this phenomenon, but so are selective publication, flexible analysis, and heterogeneity. Conversely, very large studies can detect effects too small to matter substantively.\n\nA reproducible report identifies the primary outcome, estimand, test, significance level, sidedness, target power, and assumed effect. It also states the sources and scales of variance or event-rate assumptions; allocation ratios; clustering or repeated-measure structures; expected attrition; and adjustments for multiple comparisons or interim analyses. For simulation, important additional details include the data-generating model, number of replications, random-number settings, Monte Carlo uncertainty, and handling of failed fits.\n\nSoftware and numerical conventions can affect the final integer sample size. Exact and approximate methods, continuity corrections, variance assumptions, and rounding rules need not agree. Reporting the method and its inputs makes such differences interpretable. Power curves or scenario tables can show more than a single target number, particularly when uncertainty about nuisance parameters is substantial. Where feasibility fixes the sample in advance, presenting the resulting detectable effects and precision explicitly describes the study’s capabilities without redefining a convenient threshold as a scientifically important effect."
    }
  ],
  "links": [
    "statistical-power",
    "sample-size",
    "statistics",
    "experimental-design",
    "statistical-hypothesis-testing",
    "null-hypothesis",
    "alternative-hypothesis",
    "significance-level",
    "type-i-and-type-ii-errors",
    "ronald-fisher",
    "standard-deviation",
    "sample-mean",
    "normal-distribution",
    "quantile",
    "cumulative-distribution-function",
    "standard-error",
    "students-t-distribution",
    "degrees-of-freedom",
    "effect-size",
    "odds-ratio",
    "variance",
    "publication-bias",
    "confidence-interval",
    "p-value",
    "binomial-distribution",
    "poisson-distribution",
    "linear-regression",
    "matrix",
    "analysis-of-variance",
    "statistical-interaction",
    "randomization",
    "correlation",
    "covariance-matrix",
    "multiple-testing",
    "bonferroni-correction",
    "false-discovery-rate",
    "monte-carlo-method",
    "generalized-linear-model",
    "sensitivity-analysis",
    "bayesian-inference",
    "prior-distribution",
    "posterior-distribution",
    "decision-theory",
    "confounding"
  ],
  "sources": [],
  "license": "https://creativecommons.org/licenses/by/4.0/"
}