Stated–Revealed Preference Gap

one_liner: A reported preference and behavior under a real choice opportunity systematically diverge, so the mismatch must be analyzed as two differently distorted access channels rather than automatically treating either as the agent's true valuation.

core_idea:
The stated–revealed preference gap is a systematic divergence between a valuation an agent reports and the valuation an analyst would infer from the agent's behavior under a real choice opportunity. The report may say that privacy, preventive health, retirement saving, sustainable consumption, or a proposed product matters; the observed choice may point elsewhere.

The gap does not prove hypocrisy, irrationality, or the superiority of action over speech. Both sides are measurements produced under conditions. A stated preference is elicited through wording, response options, incentives, and social setting. A revealed preference is inferred from behavior under a particular menu, cost structure, default, information state, and time horizon. Reports can be cheap and socially shaped; choices can be constrained or deliberately engineered. The divergence is therefore evidence about the two access channels and contexts, not a license to pronounce either output the agent's true valuation without further testing.

This makes the prime a triangulation structure. Align the alternatives represented in both records, verify that the same agent and focal valuation are being compared, measure the direction and persistence of the mismatch, then intervene on each channel separately. The way the gap moves reveals which distortions are doing work.

structural_signature:
- **The preference-bearing agent** — an individual or collective whose ordering is sought.
- **The focal alternatives or action** — sufficiently aligned across report and choice to support comparison.
- **The stated estimate** — an ordering or intention inferred from a solicited report.
- **The revealed estimate** — an ordering inferred from behavior under an actual menu and consequence structure.
- **The shared comparison frame** — common alternatives, time horizon, and evaluative target.
- **The systematic divergence** — rankings, choices, or magnitudes differ beyond random error.
- **The report-channel distortions** — wording, hypothetical bias, social desirability, articulation, or strategic response.
- **The choice-context distortions** — constraints, missing options, defaults, friction, salience, timing, or present bias.
- **The triangulation test** — vary one channel or context while holding the other as stable as possible and observe which estimate moves.

what_it_is_not:
- **Not hypocrisy by definition.** The report can be sincere while behavior is contextually defeated or constrained.
- **Not proof that behavior reveals the true preference.** A defaulted or high-friction choice may say more about the environment than the agent.
- **Not proof that the report is the true preference.** A low-cost hypothetical answer can be socially desirable or poorly predicted.
- **Not Knowledge-Action Gap.** That narrower prime requires correct knowledge, sincere intention, an appropriate action, and failed translation. This gap requires only aligned report and choice estimates that diverge.
- **Not Elicitation Channel Contribution alone.** A channel effect can distort one record without any opposing behavioral measure.
- **Not temporal preference reversal.** Time can cause the divergence, but the general gap also arises from constraints, framing, information, and measurement.

broad_use:
- **Digital privacy:** concern reported in surveys versus permissive data disclosure.
- **Health behavior:** stated treatment, exercise, diet, or vaccination preferences versus adherence.
- **Retirement and finance:** desired saving versus enrollment, contribution, or portfolio choices.
- **Politics:** declared priorities versus turnout, voting, donation, or migration behavior.
- **Sustainability:** environmental concern versus travel, energy, and purchasing decisions.
- **Organizations:** espoused safety or quality priorities versus enacted routines and resource allocation.
- **Product research:** claimed interest versus sign-up, payment, adoption, retention, and use.

clarity:
The prime clarifies that “preference” is not directly observed in either channel. Analysts infer it from representations. A report is a representation produced by elicitation; behavior is a representation produced by a choice environment. Their disagreement is thus not an embarrassment to discard but a diagnostic object. It can reveal which contexts activate or suppress a valuation and whether the alternatives were truly comparable.

It also separates the general pattern from named domain instances. Privacy Paradox is the digital-disclosure species. Intention-behavior gaps in health, under-saving in retirement, and survey-versus-vote differences are co-instances of the more general report-choice divergence, not metaphorical “privacy paradoxes.”

manages_complexity:
The gap organizes a sprawling list of say-do inconsistencies into a two-channel audit.

1. Align the object being valued and the time horizon.
2. Audit the stated side for hypothetical, social, strategic, and instrument effects.
3. Audit the revealed side for menu restrictions, prices, defaults, friction, information, and timing.
4. Intervene on one side at a time.
5. Treat residual disagreement as evidence of context-dependent or unstable valuation rather than forcing a single answer.

This replaces moral diagnosis with a tractable measurement and design problem.

abstract_reasoning:
Let \(P_s\) be an ordering inferred from a stated-preference channel \(C_s\), and \(P_r\) an ordering inferred from behavior in choice context \(C_r\). A gap exists when an aligned comparison function \(D(P_s,P_r)\) remains nonzero across repeated measurements or materially changes the predicted choice.

The analyst does not observe a context-free \(P\). Instead,

\[
R_s=f(P,C_s), \qquad R_r=g(P,C_r).
\]

Identification proceeds by perturbing \(C_s\) and \(C_r\). If wording changes move \(R_s\) while the choice context is stable, report-channel contribution is implicated. If reversing a default or equalizing friction moves \(R_r\) toward the report, the earlier behavior was not a clean preference readout. If the mismatch persists under both controls, context-dependent preferences, self-prediction error, or multiple evaluative systems become more plausible.

knowledge_transfer: The transfer is exact across human and organizational domains: obtain a report, observe a consequential choice, align the alternatives, measure the mismatch, audit both channels, and vary the context. Privacy researchers contribute consent-architecture tests; health psychology contributes intention-behavior and adherence designs; retirement economics contributes default reversals; product research contributes staged commitment ladders. These methods transfer because they manipulate the same report-versus-choice roles.

notes:
Authored because Privacy Paradox explicitly identifies this as its missing
cross-domain parent and existing Preference and Revealed Preference entries already
distinguish the two access modes. The alias `say_do_gap` was removed from the
unpromoted Stated Preference pilot and assigned here.


Stationarity

type: prime

slug: stationarity

one_liner: Stable statistical properties.

status: draft

core_idea: Stationarity is the property of a stochastic process or time-varying system whose statistical characteristics — mean, variance, autocorrelation, higher moments — remain invariant over time (or across translations along the relevant dimension). The essential commitment is that while individual realizations fluctuate, the generating rules do not drift: the distribution governing outcomes is the same this year as last, in one region as another<!-- FACT-D25-106 -->[^khintchine-1934]. Every stationarity claim specifies (1) the process or quantity whose statistics are being assessed, (2) the notion of stationarity being invoked (strict, wide-sense, cyclostationary), (3) the temporal or spatial window over which stationarity is asserted, and (4) the tests or evidence supporting (or challenging) the claim — because stationarity is almost always an approximation valid on some scale and invalidated by regime change on another<!-- FACT-D25-107 -->[^hamilton-1994].

structural_signature:
*the time-shift invariance of the joint distribution*
*the strict-versus-weak (covariance) stationarity distinction*
*the spectral density as frequency-domain summary*
*the autocorrelation function structure*
*the unit-root and trend-stationarity dichotomy*
*the ergodicity assumption underlying time-series inference*

what_it_is_not:
- **Not constancy.** A stationary process
  fluctuates — often substantially. The
  individual realizations are not constant; the
  statistics that generate them are. Confusing
  stationarity with constancy of values is a
  common error.
- **Not equilibrium.** Equilibrium is a state
  where net forces or gradients vanish;
  stationarity is a statistical property of
  fluctuations that persist in time. A system
  can be in a steady-state stochastic
  fluctuation (stationary) without being in a
  quiescent equilibrium; and equilibrium
  systems may have stationary fluctuations
  around them. See `equilibrium`.
- **Not ergodicity.** Ergodicity is time-average
  convergence to ensemble-average; stationarity
  is time-invariance of distribution. They are
  different properties; ergodic processes are
  stationary in a particular sense, but a
  stationary process need not be ergodic (if
  it has multiple long-lived regimes between
  which it does not mix on observed
  timescales).
- **Not absence of autocorrelation.** Stationary
  processes can have strong autocorrelation
  (AR(1) with ρ = 0.95 is stationary if ρ < 1).
  Uncorrelated does not equal stationary;
  stationary does not equal white noise.
- **Not universal validity.** Most real-world
  time series are non-stationary in some
  respect — trends, seasonality, regime
  shifts, heteroscedasticity. Asserting
  stationarity without evidence or with a
  too-large window is a classic error.
- **Common misclassification.** Conflating
  stationarity with constancy of observed
  values; treating a slowly-drifting series as
  stationary because drift is small over short
  windows; applying stationarity-dependent
  methods (ARMA models, classical spectral
  analysis) to data with unit roots or
  structural breaks.

broad_use:
- **Time-series analysis and statistics**
    - Box-Jenkins methodology (ARIMA);
      stationarity testing (ADF, KPSS,
      Phillips-Perron); cointegration;
      change-point detection.
- **Signal processing**
    - Stationary signals enable classical
      Fourier and filter-based analysis;
      non-stationary signals require time-
      frequency methods (wavelets, short-
      time Fourier).
- **Climate and hydrology**
    - Stationarity assumption in flood-
      frequency analysis and water-resource
      planning; debate around whether
      climate change has ended stationarity;
      "stationarity is dead" (Milly et al.)
      reassessments.
- **Finance and economics**
    - Returns treated as approximately
      stationary (with heteroscedasticity);
      unit-root tests in macroeconomic
      series; regime-switching models.
- **Ecology**
    - Population dynamics modeling with
      stationarity assumptions; regime
      shifts in ecosystem state.
- **Physics**
    - Equilibrium statistical mechanics as
      stationary ensemble theory; stationary
      solutions of stochastic differential
      equations; stationary turbulence
      regimes.

clarity: Stationarity clarifies by separating three questions that "stable" or "unchanging" language conflates: are values constant (no — they fluctuate), are statistics constant (the stationarity claim proper), and over what window does the claim hold<!-- FACT-D25-108 -->[^hamilton-1994]? A claim like "the market is stationary" resolves into "over the window X-Y, log returns can be modeled as drawn from a distribution whose first two moments are approximately constant and whose autocorrelation is time-invariant; unit-root tests fail to reject stationarity at the 5% level; heteroscedasticity is present (suggesting volatility clustering) but can be addressed via GARCH; the stationarity window does not extend through the 2008 crisis regime change." The clarifying force is to replace "stable" with a specifiable statistical claim bounded by window and invalidation conditions. Spectral analysis, autocorrelation functions, and formal unit-root tests (Augmented Dickey-Fuller, KPSS, Phillips-Perron) provide concrete tools for making this assessment operational<!-- FACT-D25-109 -->[^dickey-fuller-1979].

manages_complexity: Stationarity is the linchpin for reducing complexity in time-series modeling and forecasting. When stationarity holds, a large toolkit (ARMA/ARIMA models, spectral analysis, classical forecasting methods, Fourier decomposition) applies directly; when it fails, these tools systematically mislead by producing underestimated confidence intervals, missed regime shifts, and inflated forecast precision<!-- FACT-D25-110 -->[^box-jenkins-1970]. Stationarity supports generalization from past to future: a stationary process's past statistics estimate future statistics with known error bounds; non-stationary processes require explicit modeling of the drift, trend, or regime structure, which is far more demanding. Preprocessing strategies — differencing, detrending, deseasonalizing, and filtering — transform non-stationary series into stationary-in-residuals forms, making classical tools applicable to the residuals. Understanding stationarity also informs prediction horizons: stationarity claims are usually valid over specific windows (a year, a decade, a regime); knowing the validity horizon tells the analyst how far to reliably project. Climate, finance, and operational data all feature non-stationary contributions that misestimated stationary models will miss, leading to underestimated extremes and undetected regime shifts.

abstract_reasoning: Stationarity trains a reasoner to ask seven critical diagnostic questions. First: what quantity am I asserting stationarity of, and over what window<!-- FACT-D25-111 -->[^hamilton-1994]? (The same series may be stationary over one window and non-stationary over a longer one.) Second: are first and second moments (mean, variance) time-invariant? Higher moments? Joint distributions? (These differ in strength: strict stationarity requires all joint distributions to be time-shift invariant, while weak/wide-sense stationarity requires only mean and autocovariance to be stable<!-- FACT-D25-112 -->[^brockwell-davis-1991].) Third: what tests support or challenge the stationarity claim? (Unit-root tests like ADF have specific null hypotheses; KPSS tests the opposite hypothesis; examining autocorrelation decay and spectral content provides visual corroboration.) Fourth: if stationarity fails, what is the nature of non-stationarity — trend, cycle, regime shift, heteroscedasticity, long-range dependence<!-- FACT-D25-113 -->[^hamilton-1994]? (Each requires different remediation.) Fifth: can I transform the series to make it stationary in residuals, or does the non-stationarity require explicit modeling? (Differencing removes unit roots; detrending removes deterministic trends; regime-switching models accommodate structural breaks.) Sixth: what does violating stationarity mean for the conclusions I want to draw — how wrong could I be if I assume it when it fails<!-- FACT-D25-114 -->[^hamilton-1994]? (The cost depends on the application: forecasting is highly sensitive; summary statistics are less so.) Seventh: does the process exhibit ergodicity — will time averages converge to ensemble averages, or are there long-lived regimes that a single realization might miss?

knowledge_transfer:
Role mappings across domains:

- **Process / series** ↔ time series /
  signal / realization / sample path /
  observations
- **Statistics** ↔ moments / ACF / spectral
  density / distribution
- **Stationarity window** ↔ historical
  record / regime period / spatial domain
- **Strict vs wide-sense** ↔ full-distribution
  invariance / mean-covariance invariance
- **Trend** ↔ deterministic or stochastic
  drift / directional change
- **Regime shift** ↔ structural break /
  change point / state transition
- **Cyclostationary** ↔ seasonality / periodic
  modulation / repeating pattern
- **Heteroscedasticity** ↔ time-varying
  variance / volatility clustering /
  amplitude modulation

A hydrologist analyzing flood-return periods,
a quant modeling market returns, and a climate
scientist evaluating stationarity-dead climate
data are all doing the same structural work:
specify the process, choose a stationarity
notion, test the assumption, and decide whether
to use classical methods, transform the series,
or adopt non-stationary modeling. The same
diagnostic — "stationary in what sense, over
what window, with what evidence?" — applies
across their contexts, with the same failure
modes (undetected trends, missed regime shifts,
ignored heteroscedasticity) in each.

formal_abstract:
A well-behaved AR(1) process X_t = ρX_{t-1} + ε_t with |ρ| < 1 and ε_t ~ N(0, σ²) serves as the canonical stationarity example<!-- FACT-D25-115 -->[^brockwell-davis-1991]. Process: discrete stochastic time series. Stationarity notion: strict stationarity holds (Gaussian innovations and |ρ| < 1 ensure it). Mean is 0, variance is σ²/(1−ρ²), autocorrelation is ρ^k, all time-invariant. Ergodicity holds: time averages from a single long realization converge to ensemble averages. Window: valid indefinitely once ρ and σ² are fixed. Every item of the structural signature is operative and quantitatively precise. The contrast: if ρ = 1.0 (a unit-root process or random walk), the mean and variance both diverge over time, stationarity fails completely, and classical ARMA methods produce wildly misleading forecasts.

**Mapped back:** The AR(1) example embodies the Core Idea's commitment to specifying process, stationarity notion, window, and tests — all present and quantifiable.

applied_industry:
Hydrology and climate change illustrate stationarity's real-world breakdown. The historical water-resource management framework assumed that annual flood peaks were drawn from a fixed extreme-value distribution, whose parameters could be estimated from the historical record<!-- FACT-D25-116 -->[^milly-2008]. This was a stationarity claim: mean, variance, and distribution shape of peak flows remained constant. Evidence of breakdown: trend in mean and variance of peaks over recent decades, regime shifts in storm tracks, changes in snowpack timing and snowmelt dynamics under climate warming<!-- FACT-D25-117 -->[^milly-2008]. Milly et al. (2008, "Stationarity is dead") explicitly argued that water-resource planning had rested on a now-invalid assumption and must move to non-stationary frameworks. The structural kinship with the AR(1) case is precise — statistical moments, window of validity, invalidation signatures — but the substrate is climate-hydrological rather than abstract stochastic. The consequence: historical 100-year-flood estimates are no longer trustworthy for infrastructure design in a warming climate.

**Mapped back:** The hydrology case demonstrates how stationarity claims anchor operational decision-making (dam design, levee height, reservoir capacity) but can be invalidated by regime shifts that the abstract AR(1) framework models neatly in principle but which are harder to detect and respond to in real data.

prose:
_(Pass B — deferred)_

### Catalog cross-references (v1, batches 02–29)

Solution archetypes that reference this prime (per `solution_archetypes/_catalog/catalog_v1_batches_02_29.yaml`):

**As source prime (1):** `stationarity_validation`

**As related prime (5):** `adaptive_response_recalibration`, `correspondence_validation`, `layered_model_validation`, `parameter_rescaling`, `variance_reduction`

notes: Stationarity is foundational to time-series analysis, signal processing, finance, climate science, and hydrology. The concept bridges three historical traditions: classical statistical mechanics (equilibrium ensembles as stationary distributions), 20th-century engineering control theory (steady-state analysis), and modern econometrics (unit-root and cointegration theory). Key tensions arise from the finite-time nature of observations (any finite sample can appear stationary, yet longer observation windows may reveal non-stationarity) and from the invisibility of stationarity assumptions in many standard analytical methods. Contemporary applications increasingly grapple with non-stationarity: climate change undermines hydrological stationarity, regime-switching markets challenge financial stationarity, and ecosystem regime shifts invalidate ecological stationarity. The concept also maps closely to variability (which describes the magnitude of fluctuation) and to monte_carlo_simulation (which assumes stationarity of the input distributions being sampled).


Statistical Independence

one_liner: Learning one variable gives no information about another; the joint distribution factors.

origin_domain: mathematics

core_idea:
Two variables are statistically independent when learning the value of one gives no probabilistic information about the other: the conditional distribution equals the marginal. Independence is the structural absence of shared cause, shared channel, and shared history — the formal claim that two parts of a system can be reasoned about, sampled, or perturbed in isolation without bookkeeping for cross-talk. Its precise signature is a *factorization*: the joint distribution equals the product of the marginals, written $P(A \cap B) = P(A)\,P(B)$, and in the conditional form factoring given a separator set.<!-- FACT-D72-401 -->[^kolmogorov-1933]

What makes independence structural rather than a vague sense of "unrelatedness" is that the factorization is exact and testable. The claim is not that two variables seem disconnected but that the joint probability decomposes into a product, with no residual term coupling them. This sharp commitment is what lets independence carry inferential weight: under it, probabilities multiply, one variable can be intervened on without changing another's distribution, and subsystems compose with their guarantees intact. Equally important, the prime supports its own negation — *conditional dependence given Z* — which is the engine of d-separation, instrumental variables, and collider-bias diagnosis.

The pattern is recognizable wherever a system is treated as separable into parts whose behaviors do not inform one another. The variables may be coin flips, component failures, ciphertext and plaintext, asset returns, test cases, or species risks. In every instance the structural content is identical: a joint distribution that factors, and a characteristic failure when a common cause, shared channel, or hidden state reintroduces dependence and breaks the factorization.

structural_signature:
*the two or more variables (events, processes)* — *the joint distribution over them* — *the factorization claim (joint equals product of marginals)* — *the no-information-flow consequence* — *the compositional license to analyze parts separately* — *the dependence-reintroducing failure (common cause, shared channel, hidden state)*

A relation is statistical independence when each of the following holds:

- **Two or more variables.** There are distinct random variables, events, or processes whose joint behavior is in question — coin flips, component failures, plaintext and ciphertext, asset returns.
- **A joint distribution.** The variables are jointly governed by some probability law, so that "related or unrelated" is a well-posed question rather than a loose impression.
- **A factorization claim.** The joint distribution equals the product of the marginals, $P(A \cap B) = P(A)\,P(B)$ (or factors given a separator set in the conditional form). This exact, testable decomposition — with no residual coupling term — is the load-bearing invariant; it is what makes the property refutable.
- **No information flow.** As a consequence of the factorization, observing one variable leaves the conditional distribution of the other equal to its marginal: learning one shifts belief about the other not at all.
- **A compositional license.** Where the factorization holds, probabilities multiply, one variable may be intervened on without changing another's distribution, and subsystems compose with their guarantees inherited intact.
- **A dependence-reintroducing failure.** The property is broken precisely when a common cause, shared channel, or hidden state induces a residual coupling term — and the negation, *conditional dependence given Z*, drives d-separation, instrumental-variable, and collider-bias reasoning.

Composed: a factorization of the joint distribution certifies that parts may be taken separately and recombined by multiplication — a license that holds exactly until a shared cause, channel, or state reintroduces the cross-term.

what_it_is_not:
- **Not zero `correlation`.** Correlation captures only *linear* co-movement; a deterministic nonlinear relation ($Y = X^2$) can have exactly zero correlation while violating independence grossly.<!-- FACT-D72-402 -->[^feller-1968] Independence is the strictly stronger claim that the *full* joint factors, not merely that the second moment vanishes.
- **Not absence of a causal link.** Two variables with no direct causal arrow can still be dependent through a shared latent cause. Independence is a property of the joint *distribution*, not of the causal graph; a confounder breaks it without any arrow between the variables.
- **Not uniform marginals.** Uniformity describes how *one* variable is distributed; independence describes the *relation between two*. Two variables can both be uniform and tightly coupled, or both skewed and perfectly independent.
- **Not `statistical_inference`.** Inference is the *act* of drawing conclusions from data under modeling assumptions; independence is a *structural property* those assumptions may invoke (IID sampling, product likelihoods). Inference uses independence as a premise; it is not the same object.
- **Not `risk_pooling`.** Risk pooling exploits independence to make aggregate variance shrink, but pooling is the *mechanism that benefits from* independence, not independence itself. Pooling fails precisely when the pooled risks turn out to be dependent.
- **Not `orthogonality` of vectors.** Orthogonality (zero inner product) is the geometric analogue of zero correlation, not of independence; independent random variables are uncorrelated, but uncorrelated (orthogonal) ones need not be independent.
- **Common misclassification.** Reading "we found no significant correlation" as a license to multiply probabilities. Catch it by asking whether the *factorization itself* was tested, or only a second-moment summary blind to all nonlinear and conditional structure.

broad_use:
- **Probability and statistics**: the factorization is the foundational license for IID sampling, naive Bayes, bootstrap resampling, and product-form likelihoods.<!-- FACT-D72-403 -->[^casella-berger-2002]
- **Reliability and safety engineering**: redundant subsystems multiply reliability only if their failures are independent; common-mode failure (correlated outages) is the canonical violation that has wrecked nuclear, aviation, and financial fail-safes.<!-- FACT-D72-404 -->[^barlow-proschan-1975]
- **Causal inference and experimental design**: randomization is the intervention that *manufactures* independence between treatment and confounders, which is what makes the resulting comparison interpretable.
- **Cryptography and information theory**: secrecy is the demand that ciphertext be statistically independent of plaintext given no key; mutual information measures the gap from independence.<!-- FACT-D72-405 -->[^shannon-1949]
- **Software and modular design**: unit-test isolation, pure functions whose output is independent of hidden state, and fault domains in distributed systems all rely on engineered independence between components.
- **Portfolio theory and ecology**: diversification benefits depend on asset returns or species risks being uncorrelated; tail-correlation collapse during crises is the failure mode.<!-- FACT-D72-406 -->[^markowitz-1952]

clarity:
Independence reframes "no observed relationship" from a vague intuition into a precise structural claim with a testable signature: the joint distribution factors. This sharpens what would otherwise be confused with three nearby things — no causal link, no correlation, and uniform marginals — none of which is independence. A reader who has internalized the prime asks a new question of any system that looks separable: does knowing X really change my belief about Y, at all?

The clarification matters because each nearby confusion fails differently. Zero correlation captures only linear dependence and so permits strong nonlinear coupling; the absence of a known causal arrow says nothing about a shared latent cause; and uniform marginals describe one variable's distribution, not the relation between two. Independence is stronger and more specific than all of them, and naming it precisely prevents the common error of inferring separability from a weaker observed regularity. The prime's contribution is to replace a felt impression of unrelatedness with a factorization claim that can be checked — and, crucially, refuted.

manages_complexity:
Independence is the structural permission slip for compositional reasoning. A joint distribution over n variables generically requires exponentially many parameters; assert independence and the joint factors into n marginals, collapsing the exponential into the linear. Graphical models, naive Bayes classifiers, and Markov random fields are entire methodologies built on *locating* independences so that a global problem shatters into local ones that can be solved and recombined.

The same move works outside probability. Modular software is tractable precisely because each module's behavior is asserted to be independent of the others' internals, so a system of many modules can be reasoned about one module at a time. Reliability engineering buys its multiplicative gains the same way: independent failures let component reliabilities multiply into system reliability, turning a combinatorial analysis into a product. In every case the complexity independence manages is the complexity of coupling — the cross-terms that would otherwise force every part to be analyzed in the context of every other — and it manages that complexity by certifying, where it holds, that the parts may be taken separately and the results multiplied.

abstract_reasoning:
Independence lets a reasoner treat parts as separable for prediction, sampling, or perturbation, licensing three powerful moves: multiply probabilities, intervene on one variable without changing another's distribution, and compose subsystems while inheriting their guarantees. Each is a distinct structural permission, and each fails in a recognizable way when the independence assumption is wrong.

The prime also supports a rich negation. *Conditional independence given Z* — dependence that vanishes once a separator is conditioned on — is the workhorse of graphical models, the basis of d-separation, and the mechanism behind instrumental-variable and collider-bias reasoning. This means the prime carries not only a license to factor but a discipline for finding *where* factoring is valid: locate the conditioning set that renders variables independent, and the global dependency structure becomes a sparse local one. The reasoning payoff is symmetric — asserting independence simplifies, and detecting its violation (a common cause, a shared channel, a hidden state) localizes exactly where the simplification breaks and what must be modeled instead.

knowledge_transfer:
Recognizing an independence, or its violation, suggests concrete interventions that recur across substrates. A suspected common-mode failure invites diversifying suppliers, geographies, or algorithms so that failure events become approximately independent. A confounded observational comparison invites randomizing the assignment to manufacture independence between treatment and confounder. A combinatorial explosion in a model invites searching for conditional-independence structure and exploiting it through a Bayes net or factor graph. An encrypted channel suspected of leaking invites measuring mutual information between plaintext and ciphertext, where any nonzero value signals a leak. And tests that pass locally but fail in CI invite isolating fixtures, since hidden state-sharing violates the assumed independence between test cases. In every case the move from "we think these are unrelated" to "we have a factorization claim we can test" is the value of carrying the prime.

What makes these transfers genuine is the interchangeability of structural roles. *Two or more random variables, events, or processes*, *a joint distribution* over them, *a factorization claim* that the joint equals the product of marginals (or factors given a separator), *the no-information-flow consequence* that observing one cannot shift belief about the other, *the compositional license* to analyze parts separately and recombine by multiplication, and *the characteristic failure mode* in which a common cause, shared channel, or hidden state induces dependence and breaks the factorization — these map one-to-one across statistics, reliability, causal inference, cryptography, software, and finance. The cross-substrate diagnostic is a single question — does knowing one really change belief about the other? — and the cross-substrate intervention is a single recipe: where independence is wanted but absent, manufacture it (randomize, diversify, isolate); where it is assumed but uncertain, test the factorization before relying on it. The 2008 mortgage crisis, the Challenger O-rings, and a CI suite broken by shared fixtures are the same structural failure — a false independence assumption — read in three different substrates.<!-- FACT-D72-407 -->[^mackenzie-2011]

formal_abstract:
Two fair dice rolled together give the cleanest instance. The *two variables* are the outcomes $X, Y \in \{1,\dots,6\}$; the *joint distribution* assigns each of the 36 ordered pairs probability $1/36$.<!-- FACT-D72-408 -->[^feller-1968] The *factorization claim* is checkable term by term: $P(X=a, Y=b) = 1/36 = (1/6)(1/6) = P(X=a)\,P(Y=b)$ for every pair, so the joint equals the product of the marginals exactly, with no residual coupling.<!-- FACT-D72-409 -->[^feller-1968] The *no-information-flow consequence* follows: $P(Y=b \mid X=a) = 1/6 = P(Y=b)$ — learning the first die shifts belief about the second not at all. The *compositional license* this grants is what makes probability tractable: $P(\text{both even}) = P(X\text{ even})\,P(Y\text{ even}) = (1/2)(1/2) = 1/4$, computed by multiplication rather than by re-deriving a joint table. Now break it: glue the dice so $Y$ always reads one more than $X$. The marginals are unchanged, yet the factorization fails — $P(X=3, Y=4) = 1/6 \neq (1/6)^2$ — because a *shared channel* (the glue) reintroduces a coupling term. The contrast is the diagnostic the prime trains: identical marginals, identical-looking summary statistics, but one joint factors and the other does not, and only the factorization test distinguishes them. The intervention this licenses, when independence is *wanted*, is to physically de-couple — separate the channel — and re-test the product form rather than trusting that uncorrelated-looking data is independent.

**Mapped back:** The dice instantiate the full signature — two variables, a joint law, an exact product factorization, the no-information-flow consequence, and a shared-channel failure when the dice are glued — with the factorization equation itself as the load-bearing, refutable invariant.

applied_industry:
Reliability engineering of a redundant system shows the same structure with money and lives at stake, and portfolio diversification shows it again in finance. Put two backup pumps on a reactor cooling loop. The *variables* are the two failure events $A, B$; the design *assumes* independence, so system failure (both down) has probability $P(A)\,P(B)$ — if each pump fails 1-in-1000, the pair fails 1-in-a-million, the multiplicative gain that justifies redundancy.<!-- FACT-D72-410 -->[^barlow-proschan-1975] The *compositional license* is exactly this multiplication. But the factorization holds only if the failures share no *common cause*: route both pumps' power through one bus, or place both in one flood zone, and a single event takes both down together. That residual coupling term — common-mode failure — collapses the 1-in-a-million back toward 1-in-1000, and reliability built on the false product form evaporates. The same structure governs a diversified portfolio: uncorrelated asset returns let risk fall as positions are added, but in a crisis *tail-correlation collapse* reintroduces dependence — a shared channel (forced deleveraging, common funding) — and the diversification benefit vanishes precisely when it is needed. In both cases the diagnostic is the prime's single question — does the failure (or loss) of one really leave the other's distribution unchanged? — and the intervention is the same recipe: *manufacture* the missing independence by diversifying the shared channel (separate power buses, separate flood zones, uncorrelated funding sources) rather than trusting an assumed product form that a common cause can break.

**Mapped back:** Redundant-system reliability and portfolio diversification both buy multiplicative gains by asserting a factorization of failure or loss events; common-mode failure and tail-correlation collapse are the same dependence-reintroducing failure — a shared cause or channel breaking the product form — read in safety and financial substrates.


Statistical Inference

one_liner: Reasoning from a finite, noisy sample back to the underlying population or process while explicitly quantifying the uncertainty that sampling introduces.

core_idea: Statistical inference, as Cox (2006) frames it, is the reasoning by which observations on a finite sample are used to draw conclusions about an underlying population, process, hypothesis, or mechanism, with explicit accounting for the uncertainty introduced by sampling variability and model assumptions. <!-- FACT-D52-511 -->[^cox-2006] The core move, articulated already in Fisher (1925), is to treat what is observed (a sample) as one instance drawn from a probability distribution over possible samples, and to ask: what do the data tell us about the true parameters, unobserved causal structures, or future outcomes? <!-- FACT-D52-512 -->[^fisher-1925] The concept spans classical frequentist statistics (hypothesis testing, p-values, confidence intervals, likelihood methods), Bayesian inference (priors, posteriors, credible intervals, Markov chain Monte Carlo), causal inference (do-calculus, counterfactuals, instrumental variables, regression discontinuity), survey methodology, psychometrics, epidemiology, econometrics, machine learning model evaluation, A/B testing, and the replication crisis in science.

structural_signature:
Statistical inference encodes a structural pattern: **finite-data → distributional-model → parametric-uncertainty → decision-or-conclusion**. It separates what we see (the sample) from what we want to know (the population), and names the probabilistic reasoning that bridges them, a formalization Wald (1950) embedded in a unifying decision-theoretic framework. <!-- FACT-D52-513 -->[^wald-1950]

**Recurring features:**

- Generalization from sample to population under uncertainty
- Quantifying confidence through probability distributions over parameters
- Hypothesis testing and the interpretation of p-values
- Estimation of unknown parameters and their uncertainty bounds
- Causal inference and the distinction between association and causation
- Prediction and out-of-sample generalization
- Model specification and the role of assumptions
- Prior specification in Bayesian inference and its influence on posterior

The structural insight is robust, as Casella and Berger (2002) emphasize in their canonical treatment: whether estimating a treatment effect in a clinical trial, validating a machine-learning model on unseen data, inferring a disease prevalence from a sample survey, or detecting contamination in a manufacturing process, the template remains: specify a model, estimate parameters with uncertainty, and reason about what the data support. <!-- FACT-D52-514 -->[^casella-berger-2002]

what_it_is_not:
Statistical inference is **not** the same as data analysis or exploratory data analysis. Tukey (1977) characterized exploratory data analysis as a distinct mode involving visualization and pattern discovery without formal probability models or quantified uncertainty. Statistical inference goes further: it commits to a probability model and derives conclusions about parameters and predictions with calibrated uncertainty. <!-- FACT-D52-515 -->[^tukey-1977]

Nor is it identical to statistics in the broadest sense. Statistics includes descriptive statistics (summarizing a sample), design (how to collect data), and causal inference; statistical inference is narrower, focusing specifically on learning about unobserved quantities from observed data using probability.

It is also not deterministic prediction or deduction. Deduction moves from known premises to certain conclusions; inference moves from partial observations to uncertain conclusions about hidden quantities. As Neyman and Pearson (1933) framed it, a conclusion from inference is tentative, assigned a probability or confidence level, and subject to revision as new data arrives. <!-- FACT-D52-516 -->[^neyman-pearson-1933]

broad_use:
**Experimental design & hypothesis testing:** Classical null-hypothesis significance testing (NHST), Neyman-Pearson framework, power analysis, multiple comparisons corrections, false-discovery rate control.

**Clinical trials & epidemiology:** Estimating treatment effects, disease prevalence and incidence from sample surveys, attributable risk, odds ratios, hazard ratios, survival analysis, as systematized in Rothman, Greenland, and Lash (2008). <!-- FACT-D52-517 -->[^rothman-greenland-lash-2008]

**Bayesian inference:** Prior specification (informative, conjugate, weakly informative priors), Markov chain Monte Carlo (Gibbs, Metropolis-Hastings), Hamiltonian Monte Carlo, variational inference, posterior predictive checking, model comparison via Bayes factors and leave-one-out cross-validation.

**Causal inference:** Do-calculus (Pearl, 2009), the back-door and front-door criteria, instrumental variables, regression discontinuity, matching and propensity scores, difference-in-differences, synthetic control methods. <!-- FACT-D52-518 -->[^pearl-2009]

**Survey methodology & polling:** Sampling designs (stratified, cluster, systematic), weighting to population structure, margin of error, confidence intervals for proportions, dealing with nonresponse and missing data.

**Machine learning & predictive modeling:** Out-of-sample performance estimation, cross-validation, regularization, Bayesian neural networks, uncertainty quantification in predictions, calibration, evaluation metrics (ROC, AUC, precision-recall), hyperparameter selection, all developed in detail by Hastie, Tibshirani, and Friedman (2009). <!-- FACT-D52-519 -->[^hastie-tibshirani-friedman-2009]

**Econometrics & policy evaluation:** Difference-in-differences, regression discontinuity, quasi-experimental methods, inference on treatment heterogeneity, sensitivity analysis for unmeasured confounding.

**Psychometrics & measurement:** Reliability (Cronbach's alpha, ICC), validity, item response theory, latent variable models, confirmatory factor analysis.

**Quality control & process monitoring:** Inference about defect rates, process capability indices, control charts, sequential testing.

clarity:
A core function of statistical inference, as Fisher (1935) made central in his treatise on experimental design, is to name the gap between **what we observe** (a finite, noisy sample) and **what we want to know** (the true population parameter, causal effect, or mechanism). <!-- FACT-D52-520 -->[^fisher-1935] It makes explicit the role of sampling variability: different samples from the same population will yield different point estimates, and inference provides a principled framework—confidence intervals, credible intervals, p-values, posterior distributions—to quantify this variability and communicate what the data reasonably support.

This clarity also distinguishes three related but distinct tasks: **estimation** (what is the best guess at the unknown parameter?), **hypothesis testing** (is the data consistent with a specified null hypothesis, or does it provide evidence against it?), and **Bayesian updating** (given data and a prior belief, what is my posterior belief?). These approaches differ in their commitment to probability (frequentist: probability over repeated samples; Bayesian: probability over beliefs about parameters) and their interpretation of key quantities (p-values are not posterior probabilities; credible intervals are not confidence intervals).

It also clarifies why **in-sample fit is not generalization**. A model can fit observed data very well by overfitting (capturing noise rather than signal), yet predict poorly on new data. Statistical inference methods—cross-validation, regularization, information criteria (AIC, BIC)—address this distinction and provide tools to estimate out-of-sample performance.

manages_complexity:
Statistical inference, as Lehmann and Casella (1998) develop in their canonical theory of point estimation, converts vague questions like "Do we have enough evidence?" or "What is the true effect?" into formal problems: specify a probability model (e.g., Bernoulli, normal, logistic), choose an estimation method (maximum likelihood, Bayesian, method-of-moments), derive or approximate the sampling distribution of the estimator, and report a point estimate with an uncertainty bound. <!-- FACT-D52-521 -->[^lehmann-casella-1998] This formalization provides a shared vocabulary and enables systematic comparison of methods.

It also manages complexity by making hidden assumptions explicit. A simple t-test assumes independent, identically distributed (IID) normal data; a regression model assumes linearity and homoscedasticity; Bayesian inference requires a prior. By naming these assumptions, inference makes it possible to check them, revise them, and reason about robustness when they are violated.

In applied settings, statistical inference reframes stuck decision problems: instead of "Does this intervention work?", it asks "How large is the estimated effect, and how precise is that estimate?" This opens a dialogue with subject-matter expertise: practitioners can weigh the estimated effect size against minimal clinically important differences, cost-benefit analyses, or implementation feasibility.

abstract_reasoning:
Statistical inference trains intuition about **distribution thinking** rather than point thinking. Instead of asking "What is the true value?", one asks "What is the probability distribution over plausible values?" This shift enables reasoning about tail risks, interval estimation, and the properties of estimators (bias, variance, mean squared error, consistency, asymptotic normality).

It also develops capacity to reason about **power, sample size, and effect detectability**. A study may fail to find an effect not because the effect is absent, but because the sample size is too small relative to the variability and effect size (low statistical power). This reasoning applies across contexts: designing a clinical trial, planning a survey, or setting thresholds for quality-control monitoring.

Finally, it builds intuition about **the false-discovery rate and multiple comparisons**. When many hypotheses are tested, some will appear significant by chance (the garden of forking paths). Correcting for multiple comparisons (Bonferroni, Benjamini-Hochberg, or other methods) addresses this, though each has costs in terms of power. Understanding this tension enables more thoughtful experimental design and interpretation.

knowledge_transfer: The template—**sample → model → estimation → inference**—reappears across domains, a continuity Efron and Hastie (2016) trace from classical to computer-age statistics. A clinical trial estimates a treatment effect from randomized patients; an A/B test estimates the difference in conversion rates between two design variants; a survey estimates population prevalence from a sample; a sensor-fusion algorithm infers the true state of a system from noisy measurements; a machine-learning model estimates class probabilities and their uncertainty. <!-- FACT-D52-522 -->[^efron-hastie-2016] The vocabulary and methods (confidence intervals, hypothesis tests, cross-validation, Bayesian posteriors) transfer across these applications. A practitioner trained in one domain—say, clinical epidemiology—can recognize and apply techniques from another—machine learning model validation—because the underlying structure is shared.

formal_abstract:
**Hypothesis testing (frequentist):** A pharmaceutical company tests a new antidepressant against placebo in a randomized controlled trial with 500 participants. They observe a mean reduction in depression score of 8 points in the treatment arm, 6 points in the control arm, with a pooled standard deviation of 12 points. A two-sample t-test yields t ≈ 2.4, p ≈ 0.017. Interpreting this result requires care: the p-value is the probability of observing a difference at least as extreme as what was seen, if the null hypothesis (no treatment effect) were true and the study were repeated many times. The result suggests the true treatment effect is not zero, but the p-value is not the probability that the treatment works (that would be a Bayesian posterior). If the significance threshold (alpha) is set at 0.05 a priori, this result would be considered statistically significant, but statistical significance does not imply clinical significance: an 8-point vs. 6-point difference, while real, may be clinically small. **Mapped back:** This illustrates the core challenge of frequentist inference: interpreting a p-value requires distinguishing between statistical significance (a formal property of the data given the null hypothesis) and practical significance (the magnitude and meaning of the effect in context).

**Bayesian inference:** The same trial can be analyzed Bayesian. Before seeing data, the analyst specifies a prior distribution over the treatment effect, e.g., a normal distribution with mean 0 and standard deviation 5 (weakly informative: skeptical of large effects, but not dogmatic). After observing the data (8-point difference), the posterior distribution reflects both prior and likelihood: the posterior mean might be 7 points, with a credible interval (the Bayesian analog of a confidence interval) from 2 to 12 points. This posterior directly answers the question: "Given the data and the prior, what is my updated belief about the true effect?" Unlike frequentist confidence intervals, the credible interval has a direct probability interpretation: there is a 95% probability (given the data and prior) that the true effect lies in this range. The choice of prior is transparent and can be debated; different priors lead to different posteriors. This clarity is a strength, but it also makes prior specification a point of vulnerability: if the prior is poorly chosen or manipulated, the posterior inference is unreliable. **Mapped back:** This illustrates a key tension: Bayesian inference is conceptually cleaner (probability over beliefs), but it requires committing to a prior, which introduces subjectivity.

**Causal inference:** A researcher observes that people who exercise regularly have lower mortality. A naive inference ("exercise reduces mortality") mistakes correlation for causation. Instrumental variables offer a solution: if the researcher can identify a variable that affects exercise behavior but does not directly affect mortality (e.g., proximity to a new gym), then the effect of exercise on mortality can be estimated by comparing mortality across people who differ in exercise behavior because of the instrument, controlling for other confounders. Regression discontinuity is another approach: if exercise participation is determined by a clear threshold (e.g., people over age 65 receive a free gym membership), then a discontinuity in mortality at the threshold identifies the causal effect. Both methods rely on strong assumptions (no unmeasured confounding, monotonicity for instrumental variables; no unobserved confounding near the threshold for RDD), but they enable causal inference from observational data. **Mapped back:** This illustrates how statistical inference methods are tools for navigating the correlation-causation gap; each method makes different assumptions, and choosing the right method requires understanding the data-generating process and the threats to causal inference.

**Model evaluation (machine learning):** A data scientist builds a logistic regression model to predict credit default. On the training data, the model achieves 95% accuracy. But when applied to a holdout test set, accuracy drops to 78%. This gap illustrates overfitting: the model has learned spurious patterns in the training data that do not generalize. To obtain a reliable estimate of out-of-sample performance, the scientist uses k-fold cross-validation: the training data is divided into k subsets, the model is fit k times (each time leaving out one subset for testing), and the average test-set performance is reported. Cross-validation provides a less biased estimate of generalization performance than in-sample accuracy. It also enables hyperparameter tuning: different regularization strengths are tried, and the one that maximizes cross-validated performance is selected. **Mapped back:** This illustrates how statistical inference methods address the in-sample/out-of-sample gap; without such methods, practitioners might deploy models that seem to work well but actually generalize poorly.

applied_industry:
**Survey inference (polling):** A polling organization conducts a telephone survey of 1,200 voters to estimate support for a ballot measure. The survey finds 52% support, with a margin of error of ±2.8% (a 95% confidence interval: 49.2% to 54.8%). This confidence interval is derived from the sampling distribution of the proportion under simple random sampling. It means that if the survey were repeated many times with different samples of 1,200 voters, about 95% of the confidence intervals would contain the true population proportion. The margin of error is determined by the sample size, the variability of responses (higher variability → larger margin), and the significance level. If the population is heterogeneous (e.g., rural voters differ sharply from urban voters), stratified sampling can reduce the margin of error by ensuring representation of both strata. **Mapped back:** This illustrates how statistical inference quantifies and communicates the uncertainty inherent in sample-based estimation; the margin of error is a practical summary of that uncertainty.

**A/B testing (e-commerce):** An online retailer tests two versions of a product page: version A (current) and version B (redesigned). The experiment assigns 10,000 visitors to each version and measures conversion rate. Version A: 4.2% conversion (420 conversions). Version B: 4.8% conversion (480 conversions). Is the difference real or noise? A two-proportion z-test or chi-square test can assess this. If p < 0.05, the difference is declared statistically significant. However, this approach is vulnerable to multiple comparisons bias: if the experimenter checks significance repeatedly during the experiment, or if many variants are being tested, false positives inflate. Bayesian approaches or sequential testing (e.g., group sequential designs, SPRT) can address this. Moreover, statistical significance is only one criterion for action: the difference, while real, may be too small to justify the cost of implementing version B. **Mapped back:** This illustrates how statistical inference informs business decisions, but also highlights the tension between statistical and practical significance, and the risk of p-hacking when analysis is flexible.

**Reproducibility in science:** Many published studies report p-values near 0.05, suggesting either that scientists are publishing only significant results (publication bias) or that p-hacking (trying multiple analyses until one yields significance) is common. As Ioannidis (2005) argued, if there is publication bias and true effect sizes are small, many published findings will not replicate—a thesis the Open Science Collaboration (2015) corroborated empirically with a large-scale replication of psychology studies. A replication study of a published result may fail to find the effect, not because the original study was fraudulent, but because the published estimate is inflated (winner's curse: published studies are likely to report unusually large estimates by chance if true effects are small). Pre-registration (specifying hypotheses, methods, and analysis before seeing data) and open science practices reduce these problems by making it difficult to bend the analysis post hoc. <!-- FACT-D52-523 -->[^open-science-2015] This crisis in reproducibility underscores the importance of transparent, principled statistical inference.

**Epidemiology and causal inference:** A researcher studies the association between air pollution and respiratory disease. Cross-sectional data show that people in high-pollution areas have higher rates of respiratory disease. But this could reflect confounding (e.g., lower-income people are more likely to live in polluted areas and have worse health due to poverty, not pollution). To disentangle causation, the researcher uses a difference-in-differences design—a quasi-experimental approach Card and Krueger (1994) popularized in their study of New Jersey's minimum-wage increase: before and after a major factory closure in one city, respiratory disease rates are compared in the affected city versus a matched control city. If the factory closure reduced pollution and respiratory disease decreased more in the affected city than the control, this suggests causation (the factory's pollution contributed to disease). This design controls for time-invariant confounders and time-varying confounders that affect both cities equally. <!-- FACT-D52-524 -->[^card-krueger-1994] It illustrates how thoughtful study design and statistical methods enable causal inference from observational data.

title: Statistical significance and practical significance are distinct, and optimizing for one can undermine the other

body: A large study can detect tiny effects as statistically significant (p < 0.05) even if those effects are clinically or practically irrelevant. Conversely, a small study may fail to detect a large, important effect due to low power. Obsessing over p-values creates perverse incentives: a researcher might focus on achieving statistical significance rather than estimating the true effect size and assessing whether it matters. The solution requires balancing formal hypothesis testing with effect-size estimation and subject-matter judgment about practical significance.

title: The multiple-comparisons problem and the garden of forking paths create an adversarial relationship between exploration and inference

body: Exploratory data analysis (EDA) is valuable for discovering patterns and generating hypotheses. But if analyses are flexible—testing many hypotheses, trying different model specifications, excluding outliers, transforming variables—then false positives inflate (the garden of forking paths). The solution is to separate exploration from confirmation: use one dataset to explore and generate hypotheses, then test those hypotheses on a fresh dataset. Or, use multiple-comparisons corrections (Bonferroni, Benjamini-Hochberg, hierarchical testing) to adjust significance thresholds. But each solution has costs: splitting data reduces power, and multiple-comparisons corrections are conservative and reduce power further. Balancing exploration and inference is ongoing.

title: Correlation and causation are perpetually confused because standard regression captures association, not causation, yet its language invites causal interpretation

body: A regression of Y on X with a significant coefficient suggests X influences Y, but the coefficient is really a conditional association: it is the change in Y per unit change in X, holding other variables constant, under the assumption that the model is correctly specified. If there are unobserved confounders (variables that affect both X and Y but are not in the model), the coefficient is biased as a causal estimate. Methods like instrumental variables, regression discontinuity, and causal forests address this, but each requires strong assumptions. The underlying tension is that causation is not identifiable from observational data alone; it requires design (randomization) or domain knowledge (exclusion restrictions, no unmeasured confounding).

title: In-sample fit and out-of-sample generalization are in tension, and the cure (regularization, cross-validation) introduces bias and reduces power in-sample

body: A model with more parameters fits the training data better, but it may capture noise rather than signal and generalize poorly to new data. Regularization (penalizing model complexity) and cross-validation (testing on held-out data) are the standard remedies, but they come at a cost: a regularized model fits the training data worse (higher bias, lower in-sample accuracy), though it predicts better on new data (lower variance, better out-of-sample performance). The optimal trade-off depends on the problem: if the goal is understanding the data (explanation), lower regularization may be preferred; if the goal is prediction, higher regularization may be better. Choosing the right level of regularization requires subject-matter judgment and empirical validation.

title: Prior choice and prior dominance create a form of hidden influence in Bayesian inference, especially in low-data regimes

body: In Bayesian inference, the posterior combines prior and likelihood. If data are sparse (small sample size, high uncertainty), the posterior is strongly influenced by the prior; if data are abundant, the likelihood dominates and the prior has little influence (Bayesian inference "learns" the truth). In intermediate regimes, prior choice can substantially affect the posterior, and different analysts with different priors will reach different conclusions. This is a feature of Bayesian inference (transparency about prior knowledge) and a bug (different analysts can disagree). The solution is to conduct sensitivity analysis: report results under multiple reasonable priors and check robustness. But this adds complexity and requires subject-matter judgment about what priors are reasonable.

prose:
1. **Specification and estimation:** Commit to a probability model (e.g., the response is normally distributed given predictors; the outcome follows a Bernoulli distribution), choose an estimation method (maximum likelihood, Bayesian, method-of-moments), and derive the sampling distribution of the estimator (or approximate it asymptotically). Report a point estimate, a standard error, and a confidence or credible interval.

2. **Hypothesis testing and significance:** Formulate a null hypothesis (e.g., the treatment effect is zero), assume the null is true, derive the distribution of a test statistic under the null, and compute the probability of observing data as extreme as or more extreme than what was seen (the p-value). If p is below a threshold (e.g., 0.05), reject the null; otherwise, fail to reject it.

3. **Bayesian updating:** Specify a prior distribution over unknown parameters, combine it with the likelihood (the probability of the data given the parameters), and derive the posterior distribution (via Bayes' theorem). Use the posterior to make predictions or inform decisions.

4. **Causal inference:** Identify assumptions under which causation is identifiable from observational data (e.g., no unmeasured confounding, monotonicity for instrumental variables, continuity near a threshold for RDD). Use these assumptions and appropriate methods (adjustment, matching, instrumental variables, regression discontinuity, differences-in-differences) to estimate causal effects.

5. **Cross-validation and model evaluation:** Split data into training and test sets (or use k-fold cross-validation), fit a model on the training set, evaluate it on the test set, and use the test-set performance as an estimate of out-of-sample performance. Use this estimate to compare models, select hyperparameters, and diagnose overfitting.

6. **Uncertainty quantification:** Go beyond point estimates to provide intervals (confidence intervals, credible intervals, prediction intervals) or full posterior distributions that reflect the uncertainty in estimates. Report not just what the best estimate is, but how precise that estimate is and what range of values are plausible.

notes:
Statistical inference operates at multiple levels of abstraction. At the simplest level, it is a recipe: collect a random sample, compute a point estimate and a standard error, report a confidence interval or p-value. At a more sophisticated level, it involves thinking about sampling distributions, asymptotics (what happens as sample size grows), and the properties of estimators. At the deepest level, it engages fundamental questions about the nature of probability, the role of prior knowledge, and what it means to "learn from data."

The reproducibility crisis in science has thrown statistical inference into acute focus. Many published findings do not replicate, suggesting either that true effects are smaller than published estimates (due to publication bias and selective reporting), or that Type I error rates are higher than expected (due to p-hacking and multiple comparisons), or both. This has spurred reforms: pre-registration of studies, open science practices, replication studies, and more thoughtful use of p-values (e.g., the ASA statement cautioning that p < 0.05 is not strong evidence of a true effect, and that researchers should report effect sizes, study design, and other context alongside p-values).

The distinction between Bayesian and frequentist inference has softened in practice. Empirical Bayes methods estimate hyperparameters from data, blending the two approaches. Frequentist methods can be justified by appealing to Bayesian logic (deriving confidence intervals as optimal under a decision-theoretic criterion). And practitioners often use both: a frequentist analysis to test a hypothesis, and a Bayesian sensitivity analysis to explore robustness to prior specification.

The rise of machine learning has renewed interest in causal inference and out-of-sample prediction. Classical statistics emphasized estimation and hypothesis testing on carefully designed samples; machine learning emphasizes prediction on large, observational datasets. Both are important, and the integration of the two—causal machine learning, causal forests, double machine learning—is an active frontier.

Finally, statistical inference assumes that data are informative about the world, i.e., that the data-generating process has some regularity and that that regularity is reflected in the sample. This assumption breaks down if the data are systematically biased (e.g., a survey that excludes certain populations), if the world is highly non-stationary (patterns change over time), or if prior knowledge is so strong that new data provide little additional information. Recognizing when these assumptions hold is as important as the formal machinery of inference.


Statistical Power

one_liner: Probability of detecting effect.

core_idea: Statistical power is the detection-probability-for-true-effects principle that quantifies the probability a hypothesis test will correctly reject a false null hypothesis. Formally, power = P(reject H₀ | H₁ is true), equivalently 1−β where β is the Type II error probability<!-- FACT-D24-046 -->[^neyman-pearson-1933]. Power is a function of four quantities bound by a rigid mathematical relationship: the effect size δ (the true magnitude of effect under H₁), the sample size n (or equivalently the number of experimental units and allocation to groups), the significance level α (the pre-specified Type I error rate), and the variability σ (the noise in outcome measurement)—any three of these plus power determine the fourth, and power analysis is the systematic computation that makes these relationships explicit for study planning and interpretation. The concept emerged from the Neyman-Pearson 1933 framework for hypothesis testing, which explicitly formalized power as the complement of Type II error and introduced the notion of the most powerful test at a given α. Jacob Cohen's 1962 JASP paper "The statistical power of abnormal-social psychological research" and his subsequent 1969/1988 *Statistical Power Analysis for the Behavioral Sciences*[^cohen-1988] established power analysis as a systematic practice in the social sciences, quantified conventional effect sizes (small, medium, large), and provided tables and computational tools that made power analysis accessible to non-statistician researchers. The modern practice is supported by dedicated software (G*Power, PASS, R packages pwr and WebPower, SAS PROC POWER) and by routine power-analysis requirements in grant applications and study protocols. Power analysis is the pre-specified planning discipline that prevents the twin failures of underpowering (running studies that cannot detect meaningful effects, producing inconclusive results and wasted resources) and overpowering (running studies much larger than needed, detecting trivial effects as significant while consuming excessive resources)<!-- FACT-D24-047 -->[^cohen-1988]; underpowered studies are the more common and more damaging failure mode—they produce inflated effect-size estimates when they do reach significance (because only the higher-variance realizations cross the threshold, a phenomenon called the "winner's curse" or type M error; Gelman-Carlin 2014), contribute to replication failures (the original underpowered study's inflated effect cannot be reproduced by adequately-powered replications), and waste resources on null-producing studies.

structural_signature: A power analysis exhibits: (a) *a pre-specified test* — the hypothesis test whose power is to be characterized — with its test statistic, null distribution, and significance level α; (b) *an alternative hypothesis expressed as an effect-size value* δ under which power is to be computed; (c) *a probability model* specifying the sampling distribution of the test statistic under H₁ (typically a non-central version of the null distribution, parameterized by the non-centrality parameter which depends on δ, n, and σ); (d) *specification of n, α, δ, and σ* — the four quantities that jointly determine power, with three fixed and one solved for; (e) *a computational method* — closed-form formula (t-test, F-test, chi-squared), tabulated value (Cohen's handbook), or simulation-based (complex designs); (f) *design-specific adjustments* — design-effect for cluster designs, allocation-ratio for unequal-n, multiplicity-adjustment for multiple primary outcomes; (g) *sensitivity characterization* — how power varies with effect-size assumptions (because the "true" δ is unknown, power at several plausible δ values is informative)<!-- FACT-D24-048 -->[^lakens-2022]; (h) *reporting* that documents all assumptions so the analysis can be reproduced and its sensitivity understood. When these elements are properly implemented, the power analysis supports informed study design and interpretation; when they are missing or pro-forma (generic "n = 30 per group for 80% power to detect a medium effect" without justifying the medium-effect assumption), the power analysis bears little relation to actual study performance.

what_it_is_not:
- Not a post-hoc diagnostic of observed results. "Observed power" or "post-hoc power" computed using the observed effect size is a mechanical function of the observed p-value (p close to 0.05 → observed power close to 50%; p << 0.05 → observed power high) and provides no independent information beyond the p-value. The American Statistical Association and methodological literature have repeatedly criticized observed-power reporting. Legitimate retrospective analyses use pre-specified or external effect-size estimates to characterize what the study could have detected.
- Not solely about sample size. Power depends on effect size, variability, α, and sample size jointly. Increasing sample size is one lever; reducing measurement variability, choosing more efficient tests, and relaxing α are others. Design efficiency (e.g., paired versus independent designs, blocking, covariate adjustment) can substantially increase power without changing n<!-- FACT-D24-049 -->[^cox-1958].
- Not a substitute for effect-size consideration. Power analysis presupposes a specified effect size (typically the minimum clinically or practically meaningful effect). Choosing the effect size is itself a scientific judgment that power analysis cannot avoid; using Cohen's conventional "medium" effect without domain-specific justification is common but problematic.
- Not the probability that a significant result is true. This is the positive predictive value of the test (Ioannidis 2005), which depends on power, α, and the prior probability of a real effect. Power alone does not provide this value.
- Not meaningful outside the pre-specified testing framework. Post-hoc data exploration, multiple unadjusted comparisons, and analysis selection all erode the nominal α, and hence the nominal power, of any single "primary" test. Power calculations assume the analysis will proceed as pre-specified.
- Not independent of the probability model. Nonparametric tests, tests under model violations, and complex designs produce power that differs from naive normal-theory formulas. Simulation-based power is often required for non-standard situations.
- Not constant across effect-size values. The power function rises from α at δ = 0 to 1 at large δ. "80% power" is a point on this curve, not a property of the test in general. Reporting power at multiple plausible effect-size values is more informative than a single point<!-- FACT-D24-050 -->[^lakens-2022].
- Not automatically 80%. The 80% convention reflects a particular judgment about acceptable Type II error rate (20%) given typical Type I error rate (5%), implying a Type I:Type II ratio of 4:1. This ratio may or may not fit the decision context; some contexts warrant 90% or even 95% power.
- Not unrelated to publication bias and winner's curse. Underpowered studies that reach significance tend to overestimate effect sizes; this inflation feeds publication bias (selective publication of "positive" underpowered studies) and contributes to replication failures.
- Not sufficient by itself for study quality. A study can be adequately powered but have other problems (selection bias, confounding, measurement error, analysis flexibility) that undermine inference. Power is necessary-but-not-sufficient for good-quality evidence.

broad_use:
**Clinical trials and biomedicine (canonical regulatory context):** Pre-specified power-based sample-size calculation is required for most regulatory submissions. FDA Type B meetings discuss design including power assumptions. ICH E9 (Statistical Principles for Clinical Trials) addresses power, with conventional 80% or 90% power for primary endpoints. The minimum clinically important difference (MCID)—the effect size below which treatment differences are not clinically meaningful—provides the effect-size assumption for power analysis<!-- FACT-D24-051 -->[^polack-2020]. Adaptive-trial designs may modify sample size based on interim-analysis effect-size estimates (sample-size re-estimation), preserving overall power while reducing expected sample size. Non-inferiority and equivalence trials have their own power considerations, with the equivalence margin rather than zero as the target detection threshold.

**Psychology and behavioral science (canonical reform context):** Cohen's 1962 critique documented that much psychological research was underpowered (typical power of 0.18 for small effects, 0.48 for medium). Despite Cohen's tools and advocacy, power in psychology remained low through the late 20th century. The 2010s replication crisis brought renewed attention to underpowered research; meta-analyses showed median powers of 20-35% in many psychology subfields. Reform including pre-registered power analyses, power-justified sample sizes, and journal policies requiring minimum power or sample-size justification.

**Physics and particle physics:** Signal-detection power at the 5σ discovery threshold requires understanding of background rates, signal rate assumptions, and accumulated luminosity. LHC experiment design considered power at various Higgs-mass hypotheses. Dark-matter direct-detection experiment design computes power to detect signals of various cross-sections. Gravitational-wave detector sensitivity characterized through power to detect various waveform types at various distances.

**Epidemiology and public health:** Cohort-study power for detecting moderate risk ratios given disease prevalence and exposure distribution; case-control study power with fixed number of cases. Cluster-randomized trial power with design-effect adjustment for intra-cluster correlation. Vaccine-efficacy trial power—COVID-19 mRNA vaccine Phase 3 trials were explicitly powered on event rates to detect specified efficacy thresholds within event-driven trial designs. Seroprevalence surveys powered to estimate prevalence with specified precision.

**Technology and A/B testing:** Sample-size calculators are standard in experimentation platforms (Optimizely, VWO, Google Optimize, in-house tools). Minimum-detectable-effect reporting standard in test reports. Group-sequential designs allowing early stopping for overwhelming benefit or futility through power-adjusted analyses<!-- FACT-D24-052 -->[^polack-2020]. Multi-armed bandit alternatives that allocate traffic based on accumulating evidence rather than pre-specified power targets.

**Genetics and genomics:** GWAS power at genome-wide significance (5×10⁻⁸) requires enormous samples for detecting common-variant effects (often hundreds of thousands of individuals through consortia like UK Biobank, 23andMe research cohorts, Million Veteran Program). Rare-variant association tests have distinct power considerations (burden tests, SKAT). eQTL and other molecular-QTL studies powered for detecting expression effects.

**Quality control:** Acceptance-sampling plan design specifying α (producer's risk) and β (consumer's risk) with operating-characteristic curves showing power as a function of true defect rate. Process-capability study design with specified power to detect meaningful process-mean or process-variance deviations.

**Agricultural experiments:** Randomized-complete-block and factorial-design power calculations accounting for block variance and interaction structure. Long-term rotation-experiment design for detecting cumulative effects.

**Ecology and conservation biology:** Power to detect population declines of specified magnitude over monitoring periods; marine-protected-area effect-detection power; biodiversity-change detection in long-term monitoring. These often involve small sample sizes (limited sites), high variability (natural-system noise), and multi-decadal time horizons—power challenges are severe.

**Educational research:** Cluster-randomized school-trial power considering school-level intraclass correlation, typically requires 40-80 schools per arm for detectable effect sizes in the 0.10-0.20 standardized-effect range. What Works Clearinghouse standards specify minimum power thresholds for evidence classification.

clarity: The power analysis frame makes explicit the specific quantity—probability of rejecting H₀ under a specified H₁—and makes explicit the four-way relationship among power, effect size, sample size, and α. Without the frame, people run studies whose sample sizes are determined by convenience or convention without regard for what effects they can detect, interpret non-significant results as evidence of no effect regardless of achieved power, and conflate "observed power" with independent diagnostic information<!-- FACT-D24-053 -->[^greenland-2016]. With the frame, diagnosis becomes specific: What is the minimum effect size of scientific interest, and on what basis? What variability is expected in the outcome, and what data inform that assumption? What significance level is appropriate, and what power target? What sample size achieves the required power? Can design efficiency (blocking, paired design, covariate adjustment, paired-alternative designs) reduce the required n? How sensitive is the analysis to the effect-size assumption—what is the minimum detectable effect at the planned sample size? Is the study adequately powered for the primary and any key secondary analyses? If not, should the study be redesigned, or should findings be interpreted with explicit acknowledgment of power limitations? The frame clarifies that power is a study-design and interpretation parameter, not just a sample-size formula.

manages_complexity: Decomposes study design into structured components (effect size, variability, α, n, power) with explicit relationships, supporting principled trade-off analysis. Cross-domain transfer is productive: Cohen's power-analysis framework from psychology to education to medicine; design-effect-adjusted power from public-health trials to educational cluster trials to technology-platform A/B testing; sequential-design power from clinical trials to quality control to online experimentation; simulation-based power from complex-model statistics to ML evaluation<!-- FACT-D24-054 -->[^cohen-1988]. The decomposition reveals interplay with other primes: *hypothesis testing* (#434)—power is a property of the test framework; *type I / type II errors* (#445)—power is 1−β, tightly paired; *effect size* (#447)—power calculation requires a specified effect size, tightly paired; *statistical significance / p-value* (#435)—power and α jointly shape the test's operating characteristics; *confidence intervals* (#436)—CI width is the estimation-analog of power, and sample-size calculation can target CI width instead of power; *sampling representativeness* (#433)—design effect scales power; *reproducibility* (#441)—underpowered studies contribute to replication failures through winner's curse.

abstract_reasoning: The analyst asks: What is the scientific question, and what is the minimum effect size that would matter scientifically, clinically, or practically? What prior evidence informs expected effect size and variability—from pilot studies, meta-analyses, domain knowledge? What significance level α is appropriate, and what power target—80% conventional, 90% for high-stakes, something else? What sample size is required given these inputs, and is that feasible—can we collect this n, or do we need to redesign to reduce variability, use paired designs, or relax the expected minimum effect? How sensitive is the required n to the effect-size assumption—small variations in expected δ can produce large variations in required n for small effects<!-- FACT-D24-055 -->[^lakens-2022]? What design efficiencies can reduce required n—blocking, paired alternatives, covariate adjustment, matched designs? If sample size is fixed by constraints, what is the minimum detectable effect—is the study adequately powered for any scientifically meaningful effect, or is it pre-determined to be underpowered? For cluster or hierarchical designs, what is the design effect, and how does it scale required n? If running multiple tests, does multiplicity adjustment further increase required n? Mature practice conducts pre-study power analysis with domain-justified effect-size assumptions, reports sample-size justification in study protocols and publications, considers sensitivity to assumptions, and interprets results in light of achieved power. Immature practice skips power analysis, uses generic Cohen conventional effect sizes without domain justification, runs convenience-size studies, and reports "post-hoc power" as if it provided diagnostic information.

knowledge_transfer:
| Domain | Typical effect-size assumption | Typical power target | Characteristic difficulty |
|--------|--------------------------------|----------------------|--------------------------|
| Clinical trial superiority | Minimum clinically important difference (MCID) | 80-90% | MCID justification from prior evidence |
| Psychology experiment | Cohen's d = 0.5 (medium) or domain-specific | 80% | Effect-size inflation; underpowering |
| GWAS | 0.5-2% per-variant variance explained | 80% at 5×10⁻⁸ | Requires ≥10⁴-10⁵ samples |
| Cluster-randomized trial | 0.10-0.30 standardized ICC-adjusted | 80% | Design-effect doubling or tripling required n |
| A/B test (tech) | 1-5% relative lift on metric | 80% | Metric variance; sample-size vs. test-duration trade |
| Cohort study | Relative risk 1.3-2.0 | 80% | Prevalence-driven expected-event count |
| Case-control study | Odds ratio 1.5-3.0 | 80% | Case accrual; matched design gains |
| Quality control acceptance | Lot defect rate vs. AQL | Producer's/consumer's risk | OC-curve shape across lot rates |
| Ecology monitoring | 10-30% population change | 80% over N years | High natural variability; long horizons |
| Educational trial | 0.15-0.25 standardized | 80% | Cluster structure; implementation variation |

formal_abstract:
The Pfizer-BioNTech BNT162b2 Phase 3 COVID-19 vaccine trial (Polack et al. 2020, *NEJM*) is a high-profile example of power-based trial design in a high-stakes regulatory context. The trial was an event-driven Phase 3 randomized placebo-controlled trial with approximately 44,000 participants randomized 1:1 to vaccine or placebo. The primary endpoint was confirmed COVID-19 occurring at least 7 days after the second dose of vaccine. The power calculation was event-driven rather than sample-size-driven: the trial was designed to continue until a pre-specified number of COVID-19 cases accumulated across the combined trial arms, at which point the efficacy analysis would be conducted. The pre-specified success criterion for the primary efficacy analysis was that the lower bound of the 95% confidence interval for vaccine efficacy (1 minus the hazard ratio) exceed 30%—a pre-specified regulatory threshold set by the FDA for COVID-19 vaccines in October 2020<!-- FACT-D24-056 -->[^polack-2020]. Power calculation: with 164 cases across arms, the trial had approximately 90% power to rule out vaccine efficacy ≤ 30% if true efficacy was ≥ 60%; with pre-specified interim analyses at 32, 62, 92, and 120 cases, the trial could demonstrate success at interim if effects were large. The trial's final analysis was conducted at 170 cases (162 placebo, 8 vaccine), yielding an estimated vaccine efficacy of 95.0% (95% CI 90.3-97.6%), with the CI lower bound vastly exceeding the pre-specified 30% threshold. The event-driven power design illustrates several features of modern power analysis in clinical trials: (i) *Event-driven rather than fixed-sample-size* allows the trial to accumulate the number of events required for the efficacy analysis, regardless of how long it takes—particularly important during a rapidly-evolving pandemic where incidence rates were uncertain. (ii) *Sequential-analysis power* with pre-specified looks at 32, 62, 92, 120, and 164 cases, using O'Brien-Fleming-style α-spending to preserve overall Type I error near 2.5% one-sided while allowing early success at interim if effects were large. (iii) *Regulatory-threshold design* — the FDA's October 2020 guidance required demonstrated vaccine efficacy > 50% with lower 95% CI bound > 30%, shaping the power calculation around that threshold rather than around rejecting the null of zero efficacy<!-- FACT-D24-057 -->[^polack-2020]. (iv) *Large-effect sensitivity* — the trial was substantially overpowered for the observed effect size (95% efficacy vastly exceeded the 60% assumption), allowing early interim success; the design was appropriately conservative given regulatory stakes. (v) *Post-approval effectiveness* — Phase 3 efficacy estimates represent a specific population (adults meeting inclusion criteria during trial period); real-world effectiveness studies extended evidence to broader populations. The BNT162b2 trial exemplifies power analysis as practical application of the Neyman-Pearson framework at the intersection of regulatory decision-making, pandemic response, and accelerated clinical development.

**Mapped back:** This case illustrates the structural signature of power analysis—pre-specification of minimum detectable effect (vaccine efficacy ≥ 60% vs 30% regulatory threshold), event-driven sample-size determination, sequential-analysis α-spending for multiple looks, regulatory-threshold calibration—and the core abstraction that "adequate power depends jointly on α, effect size, variability, and sample size"; the event-driven design shows how power analysis applies even when sample size is random (driven by event accumulation) so long as the relationship between power and the components is pre-specified.

applied_industry:
A regional agricultural extension office is designing a multi-farm study to evaluate a new cover-cropping system intended to reduce nitrogen fertilizer requirements while maintaining yields on corn-soybean rotations in the regional climate. The cover-crop system has been tested in small-plot research-farm settings showing yield maintenance at reduced fertilizer rates, but on-farm implementation across varied soil types and management intensities is needed before regional recommendations. The extension economics and agronomy teams commission a randomized on-farm trial with the following power-driven design: (a) *Primary outcome*: Corn yield (bushels per acre) in the cover-crop system versus conventional fertilizer management, averaged across two years of the rotation. (b) *Minimum detectable difference of interest*: 5 bushels per acre on a regional baseline of approximately 190 bushels per acre (a 2.6% difference)—the extension economists judge that smaller yield differences are indistinguishable from management-variation noise and larger differences would materially affect grower adoption economics<!-- FACT-D24-058 -->[^cox-1958]. (c) *Expected variability*: Between-farm standard deviation of approximately 15 bushels per acre based on historical county-level yield variation adjusted for management; within-farm (split-field) variability approximately 8 bushels per acre based on small-plot research-farm data. (d) *Design choice—split-field versus between-farm*: Split-field design (half of each participating farm's experimental acres under cover-crop, half conventional, randomized within farm) reduces effective variability from the between-farm SD to the within-farm SD; this design-efficiency choice dramatically reduces required sample size. (e) *Power calculation*: Paired-design power with 8 BPA within-farm SD, 5 BPA target effect, α = 0.05 two-sided, 80% power target—requires approximately 24 participating farms for the 2-year rotation. (f) *Sample-size feasibility*: The extension office has commitments from 32 farms across the region, providing margin for potential dropouts and mixed-farm-size adjustments. (g) *Sensitivity analysis*: The team examines required n under variability assumptions of 10 BPA (more variable, requiring n ≈ 38 farms) and 6 BPA (less variable, requiring n ≈ 14 farms)—the 32-farm commitment covers the expected and higher-variability cases. (h) *Secondary-endpoint power*: Fertilizer reduction (clearly detectable; power near 100% at expected effect), soil-health indicators (less clearly powered at 32 farms; noted as exploratory with power caveats), and net economic return per acre (adequate power given yield-and-fertilizer primary estimates)—all documented in the analysis plan. (i) *Analysis methods*: Mixed-effects model with farm-level random effects and year fixed effects, with cluster-robust standard errors at the farm level; pre-specified sensitivity analysis using non-parametric paired tests if distributional assumptions are violated. Over the 2-year study period, the trial proceeds with 29 farms completing both years of data collection (three farms dropped due to management changes or data-quality issues—within the expected-dropout margin). Analysis: Estimated yield difference is −1.2 bushels per acre (cover-crop minus conventional), 95% CI (−4.1, +1.7) BPA. The CI includes zero and is centered near zero; the 5-BPA clinical-threshold for meaningful yield penalty is outside the CI upper bound (+1.7 < 5.0)<!-- FACT-D24-059 -->[^cumming-2014]. Interpretation: The data are consistent with no meaningful yield penalty (point estimate within 1.2 BPA of equivalence; CI upper bound well within the 5-BPA threshold of concern); the cover-crop system appears yield-neutral at the reduced fertilizer rate within the power of the study. The team's pre-specified analysis also estimates substantial fertilizer reduction (42 lbs/acre less N applied, CI tight and well-separated from zero) and positive net economic return per acre (point estimate $18.50/acre higher, CI from $4 to $33). The regional recommendation resulting from the study: Cover-crop system is recommended as yield-neutral fertilizer-reduction option for corn-soybean rotations in the region, with secondary benefits (soil health indicators, erosion reduction) consistent with research-farm findings but recognized as less fully powered. The case illustrates power analysis as practical application to agricultural field-trial design: minimum-detectable-difference specification rooted in extension-economics judgment, within-farm variability estimation from pilot data, design-efficiency choice (split-field paired) reducing required n, sensitivity analysis across variability assumptions, feasibility check against recruitment, secondary-endpoint power acknowledgment, and pre-specified analysis plan integrating effect-size estimation with power-based trial design.

**Mapped back:** This case exemplifies the structural signature of power analysis—minimum-detectable-difference (5 BPA) specification rooted in practical decision stakes, within-design-block variability estimation, design-efficiency gains from split-field pairing reducing required farm-count from ~38 to ~24, sensitivity analysis across assumed variability ranges—and the core principle that power analysis bridges experiment planning and decision-making: the pre-specified 5-BPA threshold operationalizes "what would matter," the 80% power target reflects the farmers' tolerance for missing real effects, and the final CI (upper bound 1.7 BPA) below the 5-BPA threshold allows confident conclusion of yield-neutrality.

prose:
_(Pass B — deferred)_

### Catalog cross-references (v1, batches 02–29)

Solution archetypes that reference this prime (per `solution_archetypes/_catalog/catalog_v1_batches_02_29.yaml`):

**As related prime (2):** `adaptive_threshold_recalibration`, `variance_reduction`

notes: Experimental-design/statistics origin (Neyman-Pearson 1933 formalized power as complement of Type II error; Cohen 1962, 1969, 1988 established power analysis as systematic practice in social sciences). The `tight_pair_with_type_i_type_ii_errors` flag reflects that power is 1−β, constitutive of the Neyman-Pearson framework; reciprocal flag should be wired into #445. The `tight_pair_with_effect_size` flag reflects that power analysis cannot be conducted without a specified effect size—the two primes are mutually definitional; reciprocal flag should be wired into #447. Related primes: #434 hypothesis_testing_null_vs_alternative (framework within which power is defined), #445 type_i_type_ii_errors (tight pair), #447 effect_size (tight pair), #435 statistical_significance_p_value (α and power jointly shape operating characteristics), #436 confidence_intervals (CI-precision-based sample-size planning as alternative to power-based), #433 sampling_representativeness (design-effect scales power), #441 reproducibility_replicability (underpowered studies contribute to replication failures through winner's curse), #432 randomization (randomization-based tests' power). Strong transfer targets: clinical-trial and vaccine-trial regulatory design, psychology-replication sample-size justification, GWAS multi-cohort meta-analysis, cluster-randomized-trial design across public health and education, A/B-testing platform sample-size calculators, agricultural and ecological trial design. Pass B should develop archetypes for *a-priori-sample-size-planning*, *sensitivity-to-effect-size power analysis*, *design-efficiency-through-paired/blocked-designs*, *sequential-and-adaptive sample-size re-estimation*, *cluster-design design-effect adjustment*, *simulation-based power for complex designs*, *event-driven trial power (vaccine trials, time-to-event)*, and *power-based interpretation of non-significant results*.