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The Axiomatic Trader: Latent Regularity, Information Budgets, and the Canonical Form of a Quantitative Investment System

Jiayu Li

arXiv:2608.23416v1cs.LGq-fin.PM

TL;DR

The paper asks how persistence of past trading regularities can be stated precisely when deployment is an intervention outside the historical sample. It axiomatizes a latent-state mechanism and declares five constants, then argues that the resulting information budget nearly forces the system architecture. In its tested case, tail selection bought nothing over mean selection at the readable level, while the framework remained falsifiable.

  • Problem

    The paper formalizes the assumption that past trading regularities persist through a time-invariant mechanism driven by an unobserved latent state.

    Source: Contents · p. 2

  • Method

    It defines five constants for recurrence, representation invariance, state coherence, signal magnitude, and regime dependence, then develops falsifiability tests for declared assumptions.

    Source: Contents · p. 2, §12 · p. 76

  • Results

    On the named cross-sectional test library, tail selection bought nothing over mean selection at the one level whose tail could be read.

    Source: §14 · p. 84

  • Takeaways & Limitations

    The framework treats robustness and research complexity as purchases from a finite information budget, with overdraft identified as a dominant quantitative-trading failure mode.

    Source: §14 · p. 84

    The framework leaves representation choice unresolved, and its noisy-block tail criterion has no tested remedy and cannot implement even Λ = 2’s intended penalty at the stated noise level.

    Source: §13 · p. 80

Abstract

from arXiv · show

Systematic trading rests on one article of faith: that regularities found in the past persist. We state it as a time-invariant mechanism driven by an unobserved latent state, and show that it leaves a researcher five constants to declare --- the recurrence bound $Lambda$ at a block length $b$, the invariance defect $epsilon_0$ of the representation it is declared of, the coherence times $ell_i$ of the state's coordinates, the signal ceiling $rho$ and the fraction $kappa$ of it contingent on the regime --- after which the architecture of a correct quantitative investment system is nearly forced.

A Proofs … What is not an axiom.

This section develops the paper’s axiomatic account of systematic trading by connecting five declared constants and their associated recurrence, invariance, persistence, signal, and regime-dependence conditions to system design. It also clarifies the constraints and limits of the axioms, their independence, and the separate assumptions required for deployment.

1.1 The question

  • The paper’s central claim is that a correct quantitative system is largely forced, up to constants, by five numbers describing latent-world instability.These are the recurrence bound Λ at scale b, invariance defect ε_0, state coherence times, signal ceiling ρ, and regime-contingent fraction κ.Source: §1.1 · p. 4, §4 · p. 9

1.2 The core faith and its precise form

  • The theory treats future failure as latent-state coverage failure: a time-invariant mechanism fails only when the future state mixture moves beyond the past, bounded by Λ.This reframes induction’s problem from invalid inference to unobserved states having positive future probability but zero historical coverage.Source: §1.2 · p. 4

1.3 Five declared constants

  • The five declarations specify recurrence at scale b, representation drift ε_0, persistence ℓ, signal ceiling ρ, and regime dependence κ; everything else is derived.Λ controls future reweighting, ε_0 costs 2Mε_0 in bounds, ℓ determines effective persistence costs, ρ limits conditional signal, and κ sets regime-contingent signal ρ_blk = κρ.Source: §1.3 · pp. 4–5

1.4 Contributions

  • The proofs derive worst-case selection as CVaR at level 1/Λ, unify capacity and search in a ρ^2 n_eff information budget, and charge representation search by log|Ψ|.The effective sample charges state persistence according to regime dispersion and label overlap, while adaptive search is charged in the same nats.Source: §1.4 · p. 6
  • The canonical form requires five necessary stages, fixes embargo and invariance-penalty rules, limits fractional Kelly by f* ≤ 1/(1 + κ), and averages perturbed training fits.In Experiment 14, the stages opened no positions without an edge, opened one when edge and blocks were sufficient, and never traded at exactly zero edge.Source: §1.4 · p. 6

2 Related work

  • The paper assembles classical tools into a latent-state trading theory rather than claiming market profitability, originality of each tool, or that every good procedure has the canonical decomposition.Its contribution is architectural: the axioms determine how existing ideas fit together and what procedures must account for.Source: §1.4 · pp. 6–7

3 The objects

  • The formal setup separates observable features X_t, forward returns Y_t, and unobserved states Z_t, with strategies and bounded predictive or economic losses evaluated on realized occupation paths.Past and deployment windows are represented by occupation measures, making Λ a statement about realized state frequencies rather than marginal stationarity.Source: §3 · p. 8, §3.1 · pp. 8–9

4.1 The five axioms

  • The axioms require adapted information, an approximately invariant latent mechanism, bounded recurrence, declared coherence and decoupling, and weak conditional signal.Adaptedness also requires freshness: stale carried-forward features can satisfy no-leakage while misrepresenting the state, incurring invariance defect without reducing Λ.Source: §4.1 · pp. 9–10, §4.2 · p. 10

4.2 Reading them

  • A2 makes the observable law time-invariant conditional on a declared latent state, leaving performance variation to changes in the state’s occupation measure.It permits dependence across periods and allows a positive invariance defect ε_0; conditional independence is deliberately not assumed.Source: §4.2 · pp. 10–11
  • The representation is declared before observing data because coarsening trades lower recurrence bound Λ for higher invariance defect ε_0, while refinement does the reverse.The date-plus-realisation representation achieves ε_0 = 0 but Λ = ∞, explaining everything without predicting anything.Source: §4.2 · p. 11
  • A3 requires future occupation to be dominated by past occupation at block scale, so finite Λ demands recurring atomic cells and enough blocks to cover occupied states.At block length b, K occupied cells require B ≥ K, equivalently n ≥ Kb; longer blocks give weaker promises but stronger premises.Source: §4.2 · p. 12
  • A5 caps every state-conditional trading edge at ρ, and under constant conditional variance this becomes a per-regime Sharpe ceiling SR(h⋆) = √R^2_max ≤ ρ.The same ceiling applies in each regime’s own volatility, with a remainder bounded by k_μρ^3/(2(1−ρ^2)^(3/2)); the paper calibrates ρ^2 ∈ [10^-4, 10^-2] per day.Source: §4.2 · p. 14

What is not an axiom.

  • Deployment is not an axiom: discovering a strategy adds capital as a latent coordinate, making future and past occupation singular and invalidating finite-Λ guarantees.Without a declared reflexivity model, no history-based guarantee remains; with (δ,c)-reflexivity, deployment transfers the estimate as δμ̂ − c(C,h).Source: What is not an axiom · pp. 14–15

4.3 Independence and minimality

  • The independence analysis rejects unnecessary premises: reflexivity and κ are declarations rather than axioms, while conditional independence belongs with dependence assumptions and the coupled process.A2’s declared representation and A4(i)’s coherence clause are retained because removing them would undermine the framework’s intended guarantees.Source: §4.3 · pp. 17–18
  • Under A3 and A5, κ is not free: in the Gaussian range, λ(Λ)ρ_blk ≤ (1 + Λχ_σ)ρ, with the bound giving 2.36 at Λ = 4 and χ_σ = 1.The bound is loose relative to measurements by an order of magnitude, but it constrains declarations of ρ_blk = κρ.Source: §4.3 · p. 18
  • A4 separates finite coordinate coherence times from process-level exponential mixing: a rare ladder can satisfy the latter while violating any common coherence bound below its duration.The ladder has β(k) ≤ 2e^(-k/ℓ*) while its indicator’s coherence time is at least T−2(T+1)e^(-T/ℓ*).Source: §4.2 · p. 13, §4.3 · p. 18

5 Why the axioms are necessary: an impossibility theorem

The impossibility theorem shows that recurrence protects only estimators sensitive to a 1/Λ-sized replacement, while Λ itself cannot be learned from the observable past. Consequently, choosing Λ is an unavoidable domain judgment about unseen future states.

Theorem 5.1

  • For k=⌈n/Λ⌉, an estimator insensitive to replacing k observations can be driven to its class’s worst rule with probability at least p⋆−ε_n(k).The adversarial construction preserves Axioms A1, A2, A4, and A5, satisfies A3 with constant n/k≤Λ, and changes the conditional mean by at most Δ=2ρσ̄.Source: §5 · p. 19
  • Sample-mean rankings can remain insensitive to a 1/Λ replacement, whereas block CVaR1/Λ with b≤k is designed to detect the adversarial visit.The mean statistic moves each candidate by at most 2M/Λ, while block CVaR moves by the adversarial margin less O(Λ/B), subject to a margin condition for a formal bound.Source: §5 · p. 19
  • The adversary cannot inspect the data, and the replacement cannot be shorter than one period, so smooth replace-one-stable estimators remain vulnerable as Λ grows.An estimator with replace-one sensitivity O(1/n) is ambushed with probability p⋆−O(1/n); robustness to contamination therefore reverses into vulnerability here.Source: §5 · p. 19

Corollary 5.2

  • Λ_n,m is not estimable from the observable past: its conditional law remains non-degenerate, and it equals ∞ with positive probability at every finite n.The past can provide a lower bound but never an upper bound for Λ_n,m.Source: §5 · p. 20
  • Because Λ concerns unsampled future states, selecting it is the system’s sole unavoidable domain judgment rather than an automatable statistical choice.Declining to choose Λ implicitly chooses Λ=1.Source: §5 · p. 20

6 The selection objective is derived, not chosen

The paper derives CVaR_1/Λ as the uniquely deployment-aligned selection objective implied by the recurrence bound, then extends it to noisy block scores, alternative scales, declared representations, and confidence-qualified declarations. These extensions determine how evaluation, invariance penalties, block length, representation choice, and empirical checks must be interpreted.

6 The selection objective is derived, not chosen

  • Given recurrence bound Λ at block length b, CVaR_1/Λ of historical block risks exactly upper-bounds deployment loss, is tight, and reduces to average performance only when Λ = 1.The bound increases from the mean at Λ = 1 toward the worst block risk as Λ grows; thus the selection criterion is derived from the declared belief rather than chosen by taste.Source: §6 · pp. 20–21

6.1 From block risks to block scores

  • Block scores equal block risks plus estimation noise, so purged and embargoed block evaluation is required to estimate the derived tail mean rather than a dispersion-destroyed shuffled-fold criterion.The noise is of order b^-1/2 after purging, while dependence requires coupling across blocks; random k-fold cross-validation is consistent for the target only when Λ = 1.Source: §6.1 · pp. 21–22

6.2 Invariance is priced, not preferred

  • The derived objective prices cross-regime dispersion: CVaR_1/Λ ≈ mean + λ(Λ)·sdblk, with the coefficient determined by Λ in the Gaussian regime.Mean-minus-one-standard-deviation corresponds to Λ ≈3, while one-and-a-half standard deviations corresponds to Λ ≈6; outside the Gaussian limit, the coefficient also depends on block-risk shape.Source: §6.2 · p. 23

6.3 The same belief at another scale

  • Changing block length changes the effective belief: at fixed nominal Λ, longer blocks provide less state-scale protection, so block length is not a free implementation choice.At ℓ = 60 and nominal Λ = 4, the state-scale reading falls from 2.99 at b = 60 to 1.44 at 693 days and 1.26 at 1452 days.Source: §6.3 · p. 24

6.4 The tail on a declared representation

  • Applying the tail to a declared representation fills cells by descending loss up to Λ-weighted occupancy ceilings, trading lower estimation noise against potentially lost state dispersion.At equal occupancies, representation-lattice noise is at most KHσ^2/n versus Hσ^2/b for blocks, but neither criterion dominates unless one partition refines the other; Λ > K is read as Λ = K.Source: §6.4 · p. 25

6.5 The declaration at confidence

  • Declaring recurrence at confidence 1 − ε preserves the deployment bound with probability at least 1 − ε and makes the declaration partially testable through historical window frequencies.The confidence and representation defect each cost 2Mε, while joint cell requirements raise the floor; the realized future ratio itself remains beyond what the sample can answer.Source: §6.5 · pp. 25–26

7 The information budget

This section develops an information-budget framework for decomposing and pricing the evidence used to select a strategy, including effective sample size, model capacity, adaptive search, regime persistence, and representation selection. It also delineates the framework’s limits: breadth does not remove shared regime coherence, the representation menu remains unresolved, and declared invariance requires split-sample auditing.

7.1 The effective sample

  • Consecutive periods are redundant because a horizon-H label shares mechanism noise with H−1 neighboring labels at scale σ, while persistent regimes are sampled once per sojourn at scale ρσ.Source: §7.1 · p. 26

7.2 Capacity

  • Capacity is limited by signal strength rather than state persistence: well-specified squared-loss fitting supports a fast-rate ceiling, whereas agnostic loss tightens it to d ≲ ρ^4 n_fit.The theorem’s capacity term changes by relative O(ρ²), and the fast-rate analysis is explicitly an optimistic upper bound.Source: §7.2 · p. 28

7.3 Search

  • Adaptive search is governed by information I(T; φ), not an ill-defined number of trials; for a fixed list of N candidates, the corresponding condition is I(T; φ) ≲ 1/2 ρ² n_eff with I(T; φ) ≤ log N.The Gaussian fixed-list maximum is conservative under correlated nulls, while the adaptive result applies to arbitrary selection rules and charges biased statistics separately.Source: §7.3 · p. 29

7.4 One budget

  • The unified budget charges model complexity and adaptive search through description length or mutual information, while regime persistence enters the PAC-Bayes bound through its own cumulant rather than only variance.A model with d effective parameters and a search using I(T; φ) requires roughly d + 2I(T; φ) nats; the bound separates mechanism-noise and regime-dependent clocks.Source: §7.4 · pp. 29–31

7.5 Cross-section versus timing

  • Cross-sectional breadth reduces instrument-specific noise and reducible regime dispersion but cannot increase the number of independent macro-state draws or remove common regime variance.Experiment 13 finds effective breadth 21 but a ceiling ratio of 16, with inverse-variance weighting doubling the ceiling again; the common regime component remains irreducible.Source: §7.5 · pp. 32–33

7.6 The representation is inside the account

  • Selecting among several declared representations is charged as search: each representation supplies a certificate, and the smallest certificate remains a valid bound on deployed risk.The menu’s constants Λ(ψ) and ε(ψ) are declared before observing the sample, while biased certificate estimators incur a separate bias charge.Source: §7.6 · p. 33
  • Representation selection costs log|Ψ| for reading certificates and for information revealed about the paths over which their cells average.The account therefore charges both certificate access and the path information exposed by that reading.Source: §7.6 · p. 34
  • Within a declared menu, trying both members costs log 2, but no charge resolves the menu itself or the ordering of an unordered pair.The selection currency is determined by the dearest contender and charged through proxies of the same underlying path behavior.Source: §7.6 · p. 34
  • Theorem 7.5 prices representation-dependent leakage at the constant level, while split-sample testing—not (7.7)—audits and can reject, but never certify, the declared defect.Theorem 7.5 (i) gives a charge of at most 2M + Mε(ψ), or order σ_ψ under concentration; Experiment 6’s panel D4 shows biased premises can drive selection at a price an order larger than the charge.Source: §7.6 · p. 34

8 The price of robustness … 1. An adapted, recurrence-improving feature map, with its constants declared. 𝑥𝑡= 𝜑(ℱ︀obs

This section develops the information, estimation, and dependence constraints governing robustness under latent regimes, tail-risk selection, and noisy data. It quantifies the resulting feasibility limits and shows how they shape model selection, validation, risk estimation, and the safe deployment of the canonical quantitative system.

8.1 The deployed-risk bound

  • The deployed-risk inequality decomposes error into class approximation, tail-selection noise, and contiguity, making the architecture’s five stages nearly forced.Increasing Λ raises approximation and selection costs while buying a criterion aligned with the researcher’s believed future; excess robustness can worsen both terms.Source: §8.1 · p. 35

8.2 What the tail costs

  • Robust selection costs c(Λ)^2 effective samples, so the budget condition 2c(Λ)^2 log N ≤ ρ^2 n_eff caps affordable robustness and can make it unreachable.For smooth Gaussian block risks, c(2), c(4), c(8), and c(20) are 1.17, 1.43, 1.78, and 2.47, whereas rare discrete regimes can attain c(Λ)=Λ.Source: §8.2 · pp. 36–37

8.3 Robust training is a block re-weighting

  • Robust Kelly training is ordinary training with gradients and Hessians multiplied by Λ on the worst ⌈B/Λ⌉ blocks, but it consumes Λ_fit effective samples rather than c(Λ)^2.Thus mean training with tail selection is preferred only when c(Λ)^2 < Λ_fit; the comparison depends on the observed block-risk law and fitted-class geometry.Source: §8.3 · p. 38

8.4 The third cost: reading regimes through noisy blocks

  • Block-score noise raises CVaR, creates candidate-dependent ranking bias, and stops being removable by longer blocks once b exceeds the coherence time ℓ.Experiment 6 finds the criterion’s value peaks at b = 2ℓ, while Experiment 8 attributes real-score excess over the Gaussian value to tail blocks having the largest within-block variance.Source: §8.4 · pp. 39–40
  • The noise-corrected level must narrow the tail to restore sensitivity, but it increases selection cost and requires enough blocks; otherwise nominal robust levels can perform no better than the mean.The prescription is about three times narrower than 1/Λ in the reported setting, and levels 1/8 and 1/12 are indistinguishable from 1/4 and the mean when windows contain only about four blocks.Source: §8.4 · pp. 40–41
  • At ν=7.2, the robustness ceiling is 0.674, below λ(2)=0.798, so no declared level can implement even Λ=2’s intended penalty under the measured noise.The nominal 1/4 tail achieves Λeff≈1.4, while the best achievable level reaches only 1.6–1.7; beyond the ceiling, the shortfall is a population limitation of the tail-mean criterion class.Source: §8.4 · p. 42

9 Sizing: robust Kelly and the half-Kelly fixed point

  • Full-budget sizing implies f⋆≤1/(1+κ), so κ=1 permits at most half Kelly, while full Kelly on the point estimate has non-positive expected log growth.The half-Kelly bound is a budget-utilisation consequence, not an asserted optimum: the optimal capacity utilisation is interior and the cap on f⋆ lies between one half and three quarters in Experiment 2.Source: §9 · p. 43

9.1 Deploy an ensemble, not a fit

  • Averaging fits across training perturbations preserves effective dimension while reducing estimation variance toward the class’s minimax floor, thereby raising f⋆ without spending additional capacity.For boosted trees, the ensemble should be both backtested and deployed because a single fit is highly perturbation-sensitive; Experiment 11 finds twenty ridge refits average to a single member’s dimension.Source: §9.1 · pp. 43–44

9.2 When the procedure can return a position at all

  • Experiment 11’s ledger compares 72 proposals against a library ceiling of four, leaving negative edge after the haircut, so no block length can produce a position.The two necessary bounds constrain search size and block/sample adequacy; together they show that escaping an empty daily single-asset ledger requires width across instruments rather than more history on one index.Source: §9.2 · p. 44

10 The canonical form

  • Theorem 10.2 proves that omitting any one of S1–S5 is strictly worse in some admissible world, while using all five stages attains the bound.The penalties include worst-class risk without recurrence structure, minimax capacity limits, invalid exchangeable evaluation, vanishing candidate-selection probability under unbudgeted search, and lower or negative growth under full Kelly.Source: §10 · p. 46

1. An adapted, recurrence-improving feature map, with its constants declared. 𝑥𝑡= 𝜑(ℱ︀obs

  • The canonical system declares Λ, block scale b, invariance defect ε0, coordinate coherence times ℓ_i, and invariance ratio κ, then combines adapted features, bounded shrinkage, block evaluation, budgeted search, and robust sizing.The axioms force the stages but do not uniquely determine the predictor within S2; ridge, regularised boosting, and shrunk factor models remain legitimate alternatives under the same capacity budget.Source: §1 · pp. 46–47

10.1 The three lemmas that were missing

  • The capacity ceiling is minimax: when d≥4ρ^2N, every estimator over the bounded linear class has worst-case excess risk at least one half that of the zero predictor.The result applies to arbitrary measurable estimators, including shrunk and unshrunk procedures, in the independent-observation model attaining Theorem 7.2’s rate.Source: §10.1 · p. 48
  • Below the information budget, excess risk cannot improve beyond the σ^2d/N rate by more than a constant, while d≥4ρ^2N makes learning no better than doing nothing.Here N=n/H, because overlapping labels reduce the effective sample size; the block count n/ℓ* is not the relevant budget.Source: §10.1 · p. 48
  • Shuffled folds destroy regime dispersion and asymptotically reduce shuffled-fold CVaR selection to mean selection, so the asserted Λ guarantee can fail.The contiguous-to-shuffled variance ratio is about 0.7ℓ at b=ℓ and 2ℓ−1 for b≫ℓ; in the constructed two-state example, the failure gap is (u+v)(Λ−1)p.Source: §10.1 · p. 49
  • Full Kelly is never optimal and has negative expected log growth whenever d>ρ^2n_fit, because estimation variance can exceed the signal variance ceiling.The optimal fraction satisfies f*≤1/(1+κ), with κ=d/(ρ^2n_fit), while full Kelly has g(1)≤1/2s^2(1−κ)<0 over budget.Source: §10.1 · pp. 49–50
  • The five-stage architecture is presented as necessary rather than uniquely factorized, with distinct currencies for deployed risk, prediction risk, Gaussian risk, and quadratic log growth.Cross-validation implementations may vary, and blocks with b≫ℓ soften the tail by √v(b,ℓ)/b rather than becoming literally equivalent to the mean.Source: §10.1 · p. 50
  • A tail-optimal candidate requires n≥CΛσ^2 log N/δ^2 samples in the worst case, whereas mean ranking requires n≥Cσ^2 log N/δ^2, establishing a necessary Λ−1 selection cost.The lower bound persists even when the selector observes the latent path; the additional cost of not observing the state is separate and arises from estimating the tail through noisy blocks.Source: §10.1 · pp. 50–51
  • The variance analysis separates persistent regime variation from overlap noise, with regime variance scaling through v(n,ℓ) and the overlap contribution carrying an effective H charge.For reversible chains, the redraw chain attains the worst regime variance for a fixed relaxation time, while omitted state coordinates move regime variation into the residual noise.Source: §10.1 · pp. 54–55
  • Block-scale dependence yields a sharper fitting variance σ^2d/n_fit than loose blocking bounds, because Axiom A2 preserves conditional independence while feature persistence contributes at most an ℓ_x factor.The comparison is made against E[μ(X)^2] ≤ ρ^2σ^2, producing the stated signal-to-fitting-cost relation.Source: §10.1 · p. 55
  • Robustness cannot be purchased by nominal breadth alone: shared regime factors cap effective breadth at 1/r̄, while portfolio weighting reaches its variance minimum at w ∝ A^-1 1.Equal weights are optimal only when A1 ∝ 1, and the common regime component imposes a nonzero variance floor.Source: §10.1 · p. 57
  • The selected empirical CVaR is controlled by separating pathwise latent block risk, observed block scores, and stationary population CVaR, with McDiarmid fluctuations, mixing residuals, and a convex-order bias correction.The bound requires declaring Axiom A3 at block length b, since block-averaged risk is conditionally smaller in convex order than state-level risk.Source: §10.1 · p. 58
  • CVaR selection has asymptotic variance Λ^2 Var((r−u)+) and standard deviation at most Λs, so its penalty depends on the upper-tail shape through c(Λ), not only Λ.For Gaussian tails, c(Λ)^2/Λ equals 1.363/2, 2.034/4, 3.185/8, and 6.08/20 for Λ = 2, 4, 8, and 20; c(Λ) can approach Λ when dispersion lies above the threshold.Source: §10.1 · p. 59
  • The persistent design yields an estimation floor of σ^2d/(24n_fit), while white designs can exploit vanishing overlap-spectrum frequencies and beat this rate.The bound applies to arbitrary estimators using all n labels; persistence makes the effective independent sample size a constant multiple of n_fit.Source: §10.1 · p. 61
  • Robust tail-risk selection can reverse ordinary validation: under (10.3), block CVaR prefers A even though shuffled validation eventually selects B, and the stated numbers give 0.234 versus 0.316σ_ξ.For the stated parameters, the left side of (10.3) is 0.234 and the right side is 0.316σ_ξ; as b/ℓ→∞, the left side tends to −u.Source: §10.1 · p. 62
  • The optimal robust-training fraction satisfies f⋆ ≤ 1/(1 + κ), and using the full fraction f = 1 is harmful whenever κ > 1.The result follows from s^2 ≤ ρ^2 and the Gauss–Markov floor τ^2 ≥ d/n_fit, with g(1) negative when κ > 1.Source: §10.1 · p. 62
  • In isotropic robust training, the curvature remains the ERM curvature for every Λ, while the variance inflation is Λ_fit = Λ.The level-set curvature offsets the robust tail penalty, yielding curvature ||μ||I and V_Λ = Λ Cov(g) on the tangent space.Source: §10.1 · p. 64
  • Held-out selection bias is nonnegative for affine full-sample search and is bounded by σ√(2I(T; φ)), while k actionable audits consume 2 log k nats of held-out information.The sign follows from conditional Jensen; the corresponding claim requires equal positive window weights across candidates, not candidate-specific weights or nonlinear statistics such as Sharpe ratio.Source: §10.1 · p. 65
  • Dependence-aware permutation testing has asymptotic size controlled by the covariance ratio r, while under alternatives its statistic remains separated and permutation quantiles shrink at N^-1/2.In the geometric instance, r = (2ℓ−1)/v(L,ℓ), and under alternatives D stays bounded away from zero while permutation variance is O((1 + L||δ||^2)/N).Source: §10.1 · p. 66

11 What the theory is worth against practice · 12 Falsifiability and an empirical programme

These sections recast quantitative practices as consequences of the axioms, make their information budgets and empirical limits computable, and turn the framework into a programme of refutable declarations and tests. They examine finite-window and dependence-related constraints while identifying representation choice and expressiveness as requiring separate certification.

11.1 What the accumulated practice looks like from here

  • The axiomatization explains established field practices, and Table 4 presents those independently developed practices as evidence that it captures the right structure.The section reads Part I’s objects back against practice and identifies the resulting catalogue as the main empirical support for the architecture.Source: Table 4 · p. 67, §11 · p. 67

11.2 Computing the budget: a worksheet

  • A monthly 30-year example yields a timing budget of 19 nats, with d_eff ≈5–15 and 2 log N≈16, making feature construction affordable but robust search unaffordable.The worksheet reads H, d_eff, N, ℓ, ρ, and ρ_blk from design and declarations; declaring ρ from a training-era Sharpe of 0.040 would reduce the budget to 7 nats.Source: §11.2 · p. 67
  • Real block scores follow the dear branch: c(Λ)^2≈0.9Λ for 71 timing rules, 82 long-only cross-sectional portfolios, and 19 of 20 series, while 133 published long-short signals sit at the Gaussian value.Experiments 8 and 9 attribute the excess over Gaussian pricing to heteroskedastic score noise and the bias of Proposition 8.11 (iii), showing that the dear branch concerns market-carrying block scores rather than daily data alone.Source: §11.2 · p. 68, Figure 1 · p. 68
  • The representation determines ℓ and related budget charges: slow coordinates can raise costs, conjunctions are charged near the faster coordinate, and declaring ρ instead of ρblk can change S5 openings from 38% to 0.7%.The conservative κ=1 assumption also moves the search ceiling from 4.4 candidates to 60 on Experiment 11’s series, while the section warns that computing a near-saturated budget is not validation without preregistered tests.Source: §11.2 · pp. 70–71

11.3 What the experiments check

  • Thirteen experiments separate constant checks from market evidence: six implement the axioms literally, seven use real data, and Experiment 14 tests whether the five-stage system refuses nonexistent edges and opens positions when the answer is known.The programme covers block-score pricing, effective sample size, a full declared workflow, predictions from Section 12, and a cross-sectional library.Source: §11.3 · p. 72

12 Falsifiability and an empirical programme

  • The falsifiability programme finds order-one fit and search slopes, with ℓ adding no explanatory power; CVaR is mixed, complexity half tried, tail-price blocked, and Kelly untried.Proposition 12.1 gives a distribution-free search-bias upper bound by comparing full and truncated reruns, while each kth audit spends 2 log k nats of the held-out budget.Source: §12 · pp. 72–73
  • Samples can contradict declarations but not estimate Λ: corrected invariance tests find no live-market contradiction, the exponential A4(ii) instance is contradicted, and (Λ, ε)=(4, 0.05) fails on the term spread.The split diagnostic is a curve rather than a point estimate: named coordinates produce 1.60, 1.68, and 1.68 against a null of 1.44, whereas performance-bin values remain within the null band.Source: §12 · pp. 74–76
  • At the corrected level, Experiment 7 rejects the term-spread declaration at every K by 0.024–0.067, while realised volatility is rejected only at two and three cells by 0.005–0.007.The reported lower-bound statistic uses daily excess returns and a chunked reassignment null; the null’s level is part of the verdict.Source: §12 · pp. 76–77
  • The split-halves test cannot distinguish drift from an omitted stationary coordinate, but panel H2 finds no separation slope and panel H3 makes the two-coordinate declaration consistent while increasing Λ(ψ) from 1.40 to 1.73 and 2.00.At 3 × 3 cells, the realised-volatility × term-spread declaration has nil net defect versus 0.039 and 0.028 for term spread alone, while the weighted statistic falls from 0.063 to 0.046.Source: §12 · p. 77
  • In Experiment 9, correcting the chunked null for dependence makes per-asset counts across twenty daily series fall to the false-positive expectation of the tests run, while panel H’s verdicts reduce to one row in fifteen.Source: §12 · pp. 77, 80
  • The corrected level withdraws the defect charge but not the rule against verdict-driven representation choice: term spread retains buy-and-hold edges of 8.8 and 2.5 thousandths at Λ = 2 and 4, while a nine-cell joint grid gives +4.1 and 0.0.A predeclared menu may be searched at cost log|Ψ|, but each member’s defect remains subject to the member-by-member test; refinement buys expressiveness while costing occupation.Source: §12 · pp. 77–78
  • A ten-percent state with quarterly persistence over five years has occupation floors Λ0.05 = 2.5 and Λ0.01 = 3.1, rising to 3.4 for ten cells held simultaneously.The Gaussian approximation underestimates the floor when m/ℓ is small; below m/ℓ ≈ 10, the exact bound should be used, and short histories add 1/m + 1/n noise.Source: §12 · p. 78
  • Chunk length affects permutation validity: at L = 1, the classical permutation test is anti-conservative under dependence, whereas L = 20 preserves dependence shorter than the chunk.Source: §12 · p. 79

13 Limitations and open problems · 14 Conclusion

The paper closes by identifying unresolved theoretical, representational, and market limitations while arguing that quantitative research is governed by an explicit information budget. Its framework is falsifiable, prescribes how to spend that budget, and remains supported on some procedural tests despite mixed evidence on its predictions.

13 Limitations and open problems

  • The paper’s central limitation is that its worst-case guarantees and several closed forms rely on bounded losses, declared representations, or one-chain results rather than general market conditions.The text lists eighteen limitations, including heavy-tailed returns, one-chain derivations, uncomputed divergences, and unresolved effective-sample assumptions.Source: §13 · p. 80, §13.1 · pp. 80–81

13.2 The tail read through noisy blocks

  • No tried remedy removes the noisy-block tail bias: its usable narrowed-level range is capped, with Λeff ≈1.4 nominally and no declared level exceeding approximately 1.7.The unresolved problem is a criterion that reads regime tails without passing through noisy block-score means; reweighting by block noisiness discounts stressed blocks.Source: §13.2 · p. 81

13.3 The status of the axiomatisation

  • The axiomatisation leaves representation choice, state scale, axiom minimality, heteroskedastic constants, and the relationship between declared and calibrated signal ceilings unresolved.Finite Λ forces a finite latent space, but the ε(ψ)–Λ(ψ) trade and appropriate partition scale are not identified; the canonical form is a necessity theorem rather than a factorisation.Source: §13.3 · pp. 82–83

13.4 The market side

  • The market-side model omits an endogenous treatment of reflexivity and a transaction-cost-aware budget, although measured costs reduced the declared signal ceiling by only 3.5% in Experiment 11.Reflexivity was summarized by one publication-biased decay number, while transaction costs are charged once in S5 rather than integrated throughout the budget.Source: §13.4 · p. 83
  • On the one real series, Λ = 4 produced no robust position, while the framework can open positions when the edge is sufficiently large and does not open them on null worlds.Experiment 11 found no candidate position under the dispersion penalty; Experiment 14 opened a position with a large edge and none on a null world.Source: §13.4 · p. 83

14 Conclusion

  • The framework interprets persistence through an unobserved state, with Λ governing sample-to-world differences, ℓ governing duration, and ρ limiting signal strength and supported research complexity.For single-asset daily research, the conclusion gives limits of a few dozen nats on the mean and two dozen quarter-tail configurations before decay is charged.Source: §14 · p. 84
  • Robustness is an information-budget purchase: selecting on the 1/Λ tail divides effective sample size by c(Λ)^2, making budget overdraft the paper’s dominant failure mode.The proposed response is to buy breadth, shorten horizons, improve labels, pre-commit searches, shrink, deploy averages, and report performance as a function of Λ.Source: §14 · p. 84
  • The framework’s predictions received mixed evidence: P2 held in one test, P1 failed on the named cross-sectional library, and the procedure remained inactive on null worlds.Experiment 12 supported P2, while Experiment 13 found no tail-selection advantage and Experiment 14 found no false openings or null-world positions.Source: §14 · p. 84

B Experiments

The experiments test the paper’s five-stage quantitative system across controlled chains, simulations, and published financial data. Results support its dependence on block-aware validation, information-budget penalties, coherence scaling, and tail-risk correction, while exposing limits of debiasing and invariance declarations.

Controlled selection and capacity

  • At Λ ≥4, mean selection deploys a rule with future return −16.8 while block-CVaR remains +57.5 × 10^-3, and the exact optimum uses 0.33–0.94 of the signal ceiling.The optimum follows ρ2n/H despite feature persistence and regime flips.Source: B Experiments · p. 90

Dependence and coherence

  • Block-aware experiments use blk_v(n, ℓ) rather than max(ℓ, H), recover product-rate interaction costs, and yield a PAC-Bayes bound 1.11 times the Gaussian value.The ladder mixes quickly while its indicator has coherence time T.Source: B Experiments · p. 90

Tail-risk training

  • Block-level CVaR training rescues a losing rule once bud/Λ exceeds about 3, whereas row-level CVaR never beats ERM and Λfit tracks Λ within 5%.These results compare row- versus block-level training and assess recovery of the dependence parameter without fitting a constant.Source: B Experiments · p. 90

Tail price

  • The tail-price formula matches to three decimals, but the ranking deficit decays only as b^-0.41; a level about three times narrower is the only effective lever.At measured calibration, the resulting ceiling remains below λ(2).Source: B Experiments · p. 90

Cross-asset validation

  • Across 20 assets, raw ĉ(4) exceeds Gaussian on 19, studentised values do not, and the excess decays as b^-0.53; the term spread is contradicted on 14 of 16 equities uncorrected.The residual contradictions are two matrix-priced bond funds, while the tail criterion’s excess degradation matches plug-in ĉ(Λ′).Source: B Experiments · p. 91

Scaling and published signals

  • The broader evidence finds median variance ratio υ = 0.86, fitted coefficient variance tracking H rather than ℓ*=60, and search slopes 0.79 and 0.66 for derived scaling laws.A 72-way search exceeds its budget, with an overdraft bounded at 0.86 annual Sharpe; published signals show a 21.3 versus 1.6 breadth contrast and post-publication decay of 0.44.Source: B Experiments · p. 91

B.1 Experiment 1: the selection objective

Experiment 1 shows that under a more stress-heavy future, contiguous block-CVaR selection remains profitable while mean-based selection deploys a losing strategy; shuffled-fold CVaR loses this regime-sensitive behavior. The results also show that longer blocks reduce, but do not eliminate, regime-dispersion effects.

Selection objective

  • At Λ = 4, mean selection produces negative expected future return, whereas CVaR1/4 on the same candidates yields +0.057 per period.Mean selection always chooses θ̄ = 0.561, while CVaR selection remains positive but does not reach the oracle.Source: Table 8 · p. 92, §B.1 · p. 92
  • Shuffled-fold block-CVaR selects θ̄ = 0.51–0.56 versus 0.22–0.25 for contiguous blocks, with stress-occupation variance 0.0022 versus 0.0655.The resulting variance ratio is 29.3, close to the 29.4 predicted by (7.1), explaining why shuffled folds behave like the mean.Source: §B.1 · pp. 92–93
  • CVaR separation ranges from 23.4 to 55.7 × 10^-3 across Λ = 1.5–8, versus 20.0 × 10^-3 for the mean.The separation ratio is 1.2–2.8, so the tail criterion has more selection margin wherever it differs from mean selection.Source: §B.1 · p. 93
  • At Λ = 4, block-CVaR shortfall is 28.2%, 31.6%, and 36.5% for b = 40, 150, and 300, while the mean remains at 121%.Stress-occupation variance falls from 0.0655 to 0.0203 as b increases, matching Proposition 10.4(i), while the selected rule remains unchanged.Source: §B.1 · p. 93

B.2 Experiment 6: the price of the tail

Experiment 6 identifies a third tail cost: block-score noise and representation choice can dominate robust training’s Λ and selection’s c(Λ)^2, while narrowing the nominal tail level offers only limited relief. The experiments quantify these costs, locate an interior block-length optimum, and test representation and block-length prescriptions.

Panels A–B

  • For smooth risks, c(Λ) tracks Λ1/4 within 3% through Λ = 5, while rare discrete regimes cost Λ2 and make c(Λ) nonmonotone.At Λ = 4 and N = 104, tail ranking returns 0.063 versus 0.055 for mean ranking on B/c(Λ)^2 blocks, compared with 0.268 at Λ = 1.Source: §B.2 · pp. 93–94, Table 9 · p. 93

Panels C–D

  • At B = 315, CVaR selection returns 57.5 versus an oracle’s 80.0, while exact block signals recover 79.4, revealing persistent errors-in-variables bias.The shortfall decays as b−0.41; with ℓ = 40, value peaks at b = 80 = 2ℓ (60.2) and falls to 46.7 at b = 1280.Source: §B.2 · p. 94, Table 10 · p. 94

Panels E–G

  • Narrowing the nominal level from 1/Λ to 1/(3Λ) improves selection, whereas studentising is dominated and widening the level worsens performance.Under Student-t score noise, 1/12 works in every cell while six blocks do not, making the prescription narrower by about three rather than fifty.Source: §B.2 · pp. 94–95, Figure 3 · p. 95

Panel J

  • 0.674 and 0.627 are the measured sensitivity ceilings versus λ(2) = 0.798, so no declared level implements even Λ = 2’s intended penalty.The nominal 1/4 implements Λeff = 1.4, the best level implements 1.6–1.7, and Λ′ = 12 collects 93–100% of the available improvement.Source: §B.2 · p. 95

Panels D2 and D4

  • At b = 40, the declared two-cell representation returns 74.6 versus 56.9 for the block criterion and an oracle’s 80.0, but purity 0.20 is worse than the mean.The menu selects cells at every purity; at purities 0.33 and 0.20, false cell optimism costs 13.6 and 47.6, exceeding the log 2 selection charge.Source: §B.2 · pp. 95–96

Panel H

  • With ℓ = 40 and n = 12,600, increasing b from 40 to 600 lowers the block-CVaR pick from 57.5 to 42.6 versus an oracle near 80.0.The prescribed block length costs B through finite- B tail sampling, rather than introducing another cost beyond the tail criterion.Source: §B.2 · pp. 93, 96

B.3 Experiment 5: robust training versus robust selection

Experiment 5 shows that robustness depends on selecting tail blocks rather than individual observations: block-level CVaR can rescue training, whereas row-level CVaR does not. The results also support the budget-ratio condition and show that the training-cost factor is close to the theoretical scaling.

B.3 Experiment 5: robust training versus robust selection

  • 0.0712 versus 0.0674 at Λ = 2 and budget 100.8: robust variants finally exceed ERM, while both lose to ERM at budgets ≤25.2.At Λ = 4, block-CVaR turns negative ERM positive once bud/Λ is about 3, with gains increasing from −0.0008 to +0.0348; row-level CVaR reaches only 0.0001 versus 0.0348.Source: Table 11 · p. 96, §B.3 · p. 97
  • Block-level CVaR training changes the objective over tail blocks, while row-level CVaR behaves like ERM on a smaller sample and fails to deliver robustness.The experiment uses two latent regimes with mixing time ℓ = 40, sign-flipping coordinates in the rare regime, and exact expected future Sharpe ratios.Source: §B.3 · pp. 96–97
  • 0.0039 versus 0.0038 at b = 300 shows that changing the number of blocks leaves results nearly unchanged; which blocks define the tail matters instead.This reproduces the first table within Monte Carlo noise for the ρ = 0.20, Λ = 4, n = 12, 600 row.Source: §B.3 · p. 97
  • 0.840 versus 0.796 at Λ = 1 and 1.681 versus 1.595 at Λ = 2 show that the sandwich prediction prices training accurately on the control.The fitted ratio Λfit tracks Λ, while the rare-regime law gives 2.14 at Λ = 2; the margin Λfit/c(Λ)^2 is 1.5 to 2.1 rather than Λ.Source: §B.3 · p. 97

B.4 Experiments 2–3: the arithmetic

Experiments 2–3 test the paper’s arithmetic across capacity, search, rare-regime, and off-redraw settings. The results support coherence-adjusted effective sample sizes, distinguish budget limits from covariance-spectrum collapse, and validate the proposed variance and tail bounds.

Capacity

  • d⋆=3, 8, 45 at H=60, 10, 1, versus observed 3, 5, 20, while varying ℓx and regime loadings confirms the coherence-adjusted capacity rule.At H=10, ℓx=250 gives d⋆=8 and ℓx=10 gives d⋆=5 because m falls to 0.65; half the loadings flipping makes the regime term invisible.Source: §B.4 · p. 97
  • 0.004–0.015 out-of-sample Sharpe at d=199 against n/ℓx=210 shows persistent-feature failure is caused by the Marchenko–Pastur edge, not budget saturation.Exact-optimum budget utilisation is between 0.94 and 0.33, while the Kelly fraction is capped between 0.52 and 0.75.Source: §B.4 · p. 97

Search

  • 0.997, 0.81, and 0.47 genuine-strategy discovery probabilities at N=10, 104, and 10^6 validate the effective-sample-size search prediction, with substantially lower probabilities for monthly labels.At monthly H=21, probabilities are 0.51 at N=10 and 0.25 at 50; using the block-level neff=83 gives 0.31 and 0.11.Source: §B.4 · p. 97
  • 1.11 times the Gaussian value is the worksheet tail-bound ratio, while the extremal-regime root is 1.04–1.40 times the quadratic approximation across λmℓ=0.05–0.5.The root improves on the Bernstein form over the reported range and varies with coherence, volatility, and sample size.Source: §B.4 · p. 98

The rare ladder

  • 19.6, 40.0, 80.0, and 160 are the ladder indicator’s coherence times at T=20, 40, 80, and 160, matching the supremum over functions rather than the mixing-rate declaration 2ℓ∗−1=9.The lag coefficients peak at 0.18, 0.09, 0.05, and 0.001, satisfying the declared exponential Axiom A4(ii) instance with β0=2 to spare.Source: §B.4 · p. 98

Off the redraw chain

  • 2.56, 4.36, 1.18, and 22.16 match Lemma 7.1’s predictions on the ladder, while two-scale additive rows agree within 4% and the interaction row gives 2.59 versus 2.64.The interaction is governed by the combined scale ℓ12=9.65 rather than the slower coordinate; coverage probabilities also approach the coherence-time Gaussian floor across windows.Source: §B.4 · p. 98

B.5 Experiment 7: the constants on one real daily series

Experiment 7 estimates the widest constant, c(Λ), across 71 untuned timing rules on one 1997–2026 daily equity-index series. Real block scores favor the heavy-tailed, left-skewed branch over the Gaussian alternative, while representation choice materially changes measured signal and declarability.

Design

  • The experiment applies the plug-in ĉ(Λ) to standardized 60-day block scores from 71 untuned rules over 7,454 daily observations, reporting only the cross-rule distribution.The sample spans 1997–2026 with B = 124 blocks, and includes moving-average, momentum, reversal, volatility-target, VIX, yield-curve, long–short, and conjunction rules.Source: §B.5 · p. 98

Main result

  • c2/Λ is 0.9–1.1 across all levels, versus 0.68, 0.51, 0.40, and 0.30 for Gaussian scores, while buy-and-hold gives ĉ(4) = 2.41 with a 90% interval [1.80, 2.83].The score law is left-skewed and heavy-tailed, with median skewness −0.53 and excess kurtosis 1.92; Panel A is the result admitted to the argument because it changes the expected branch.Source: §B.5 · p. 99, Table 12 · p. 99

Open quantities

  • Noise-to-signal is 6.6, while consecutive block-score autocorrelation is −0.01 against a permutation null of ±0.08, implying median ρ²_blk = 0.0009.The block-score coherence time is near one: median τψ is 1.05 at Λ = 4 and 1.00 at 1/12, against a permutation-null value of 1.00.Source: §B.5 · p. 99

Alternative representation

  • Quantile-cell representations reduce sampling noise and dispersion, but their selector values remain statistically indistinguishable from block CVaR1/4, with comparison differences 0.29–0.69 versus 0.53.At K = 2 and 3, cell-mean sampling error is 0.70 and 0.86 of the median candidate edge, versus 5.5 for block scores; noise-removed cell-risk dispersion is 0.2–1.5 of block-risk dispersion.Source: §B.5 · p. 99

Two-coordinate declaration

  • At matched cell counts, buy-and-hold changes from +8.8 and +2.5 on ten term-spread cells to +4.1 and 0.0 on nine joint volatility–term-spread cells, while retained dispersion is 0.85 versus 0.87.The joint declaration raises cell-mean sampling error from 0.86 to 1.49 times the median edge; the shift reflects how the joint grid unbundles high-volatility crash-and-recovery days.Source: §B.5 · pp. 99–100

Declarability and coherence

  • Five-year windows make Λ = 4 fail on the term spread in three of five windows, while the declared coordinates’ long-lag dependence and embargo bounds require horizons of 390, 530, and 550 days.For realised volatility, log VIX, and term spread, the first embargo gaps reaching the 0.10 tolerance are respectively 390, 530, and 550 days; the term spread’s effective visits are below one at the five-year horizon.Source: §B.5 · p. 100

B.6 Experiment 8: taking the measurement apart

Experiment 8 shows that measurement-error de-biasing can recover latent-law features only when noise is limited, while severe convolutional noise destroys information regardless of sample size. On the real series, Experiment 7’s excess tail statistic reflects volatility clustering in score noise rather than the market’s unmeasured block-risk law.

Experiment 8: taking the measurement apart

  • The experiment compares SIMEX and heteroskedastic Gaussian-mixture deconvolution against known-truth simulations before applying them to the real rules.It evaluates four latent laws at noise-to-signal variance ratios 0.25, 1, and 6.6 with B=124 and 200 replications, repeating the design at B=1000.Source: §B.6 · p. 100
  • At noise-to-signal variance ratio 6.6, neither estimator identifies the latent law: the plug-in reads 1.5 for every law, and B=1000 does not recover the lost information.When noise variance is at most the block-signal variance, de-biasing costs 2–6 in blocks; the mixture recovers 3.25–3.32 versus 3.30 and 2.55–2.61 versus 2.66, while SIMEX closes about half the gap.Source: §B.6 · p. 101
  • At b=60, the raw block-mean tail pays c2 ≈0.9Λ, but the observed excess c(Λ) is attributable to volatility clustering in estimator noise, not the market’s block-risk law.Noise variance correlates −0.26 with score and +0.50 with score magnitude; studentisation reduces median excess kurtosis from 1.92 to 0.08, with the plug-in at or below the Gaussian form at every level.Source: §B.6 · p. 101

B.7 Experiment 9: twenty assets, seven block lengths · B.8 Experiment 10: the effective sample, measured

Across twenty assets and seven block lengths, raw non-Gaussianity disappears with aggregation while studentised statistics remain at reference, and measured effective samples greatly exceed conservative block-level charges. The experiments also find limited invariance evidence, quantify tail-selection optimism, and show that shared regime paths constrain cross-sectional inference.

B.7 Experiment 9: twenty assets, seven block lengths

  • At b=60, candidate-median ĉ(4) exceeds Gaussian 1.43 by more than 0.1 on nineteen of twenty assets, but studentisation restores the reference and lowers excess kurtosis.Raw medians range 1.43–2.18 versus buy-and-hold 1.48–2.74; studentised values are within 0.1 of 1.45 or below it, while pooled excess kurtosis falls from 1.1–10.8 to −0.57–0.30.Source: §B.7 · p. 101
  • Raw excess decays as b^-0.53 and vanishes at one year, while studentised plug-in values stay at or below reference across all block lengths.Variance beyond ten-day dependence is indistinguishable from zero from one week to one year, and Experiment 7’s 6.6 ratio is a lower bound because its Newey–West floor is biased down.Source: §B.7 · p. 102, Table 14 · p. 102
  • Single-best selection reaches out-of-sample Sharpe 0.51 versus 0.18–0.39 for robust criteria, while equal-weighted top-ten selection reaches 0.40 versus 0.45–0.53; nothing clears |t|=2.With nineteen yearly windows, Sharpe-difference standard errors are 0.25–0.3, and correlated assets and rules share one regime path, leaving the library with one asset’s worth of regime draws.Source: §B.7 · p. 102
  • The invariance correction leaves only two equity positives for the term spread, one for the pair, and none for realised volatility, consistent with the expected 2.4 false positives.The corrected defects are 0.002–0.011 for the term spread and 0.008–0.068 for two matrix-priced bond funds, whose NAV staleness is treated as measurement.Source: §B.7 · p. 102
  • Tail-selection excess degradation ratios are 1.97 at ĉ(4)=1.82 and 2.92 at ĉ(12)=2.82, versus Gaussian controls 0.90 and 1.41.The 1/4 ratio moves +0.95 between levels against a predicted +1.00, while one shared regime path limits cross-library ordering power; the 1/12 ratio falls toward the plug-in as N grows.Source: §B.7 · pp. 102–103

B.8 Experiment 10: the effective sample, measured

  • Measured effective-sample ratios are 0.92, 3.7, 13.9, and 35.7 at H=1, 5, 21, and 63, tracking H at 0.6–0.7 of its value and never approaching 60.For the median asset, n=6830, neff≈8000, and tail-term neff/ĉ^2≈2400, versus n/60=115; corresponding budgets are 68 nats for fitting, 80 for mean search, and 24 for quarter-tail search.Source: §B.8 · p. 103
  • Daily dependence is generally negative rather than a large persistence penalty: S&P 500 autocorrelation is −0.082 at t=−7.2, with negative autocorrelation on sixteen of twenty series.The median rule’s variance ratio is 0.86, while the declared ceiling implies an upper bound of 2.20; only the high-yield fund reaches 3.3, so conservative ledgers should still charge max(H, υ̂).Source: §B.8 · p. 103

B.9 Experiment 11: the five stages walked once

Experiment 11 walks S1–S5 once on committed data with constants declared before computation and records each stage’s information budget. The walk finds that the search is over budget and that the resulting haircut eliminates every candidate’s position at the declared Λ = 4.

Design

  • The experiment executes S1–S5 sequentially on precommitted training, embargo, and held-out eras, using declared constants and a ledger line for each stage.Training spans 1997–2016 with n = 5034 days; the held-out era contains 1897 days and is read once by S4.Source: §B.9 · pp. 103–104

S4 audit

  • The 72-candidate search exceeds the 23.0-nat search budget at the criterion’s actual level, leaving only fifteen Gaussian-priced or four plug-in-priced candidates affordable.The fit spends 25.2 of 50.3 nats, while the search charge is 23.0 nats; the full rerun selects a rule with held-out Sharpe 0.81 versus −0.04 for the truncated search.Source: §B.9 · p. 104

S5 position rule

  • Every candidate’s robust edge crosses zero between Λ = 1.1 and 1.3, so no library candidate has a position at the declared Λ = 4.Figure 4 places the split estimate at Λ̂split = 1.36, the held-out p = 0.1 floor at Λ0.05 = 2.24, and the self-consistent p = 1/Λ fixed point at 1.17.Source: §B.9 · p. 105, Figure 4 · p. 105

Panel F

  • The compounding check recovers the predicted fraction 1/(1 + κ): OLS gives 0.775, 0.650, 0.475, and 0.325 at κ = 0.25, 0.5, 1, and 2.These values are within one grid step of the prediction; shrinking the ridge optimum again by 1/(1 + κ) sacrifices 3% of growth at κ = 1/4 and 45% at κ = 2.Source: §B.9 · p. 105

Overall verdict

  • The haircut alone permits fewer than 4.4 proposals at the selected rule’s edge and effective sample, versus 72 compared, so no block length produces a position.At the measured dependence, the search budget is 45.5 nats and the Gaussian charge fits with 9.5 nats to spare, while the plug-in charge is −32 nats.Source: §B.9 · pp. 105–106

B.11 Experiment 13: the cross-sectional library

Experiment 13 tests the theory on two cross-sectional libraries with sharply different effective breadth, showing that regime variation, block-score structure, and publication-time decay materially qualify what breadth and selection can deliver. The field’s corrections broadly agree with the budget’s haircut, while adding an explicit clock, tail layer, and ex-ante sign.

Panel A, breadth

  • The long-short library’s effective breadth is 21.3 versus 1.6 for long-only, yet its equal-weight ceiling ratio is 16.4 rather than the breadth-only 29 because regime variation remains.Average pairwise correlations are 0.052 and 0.660, respectively; inverse-variance weighting raises the long-short ceiling ratio to 37, while common regime variance remains at most 0.003.Source: §B.11 · p. 107

Panel B, the plug-in

  • At b = 12 months, the long-only library has median ĉ(4) = 1.88 versus Gaussian 1.43, while the long-short library gives 1.46 at Λ = 4 and both studentised values collapse near Gaussian.At Λ = 20, the two libraries’ ĉ2 ratio is 2.1, supporting the claim that the dear branch belongs to block scores carrying the market rather than daily data.Source: §B.11 · p. 107

Panel C, P1

  • P1 produces no usable tail benefit where it can be read: the long-only deployed block tail improves by at most +0.13, while long-short changes remain below 0.08.The long-short 1/8 Sharpe deficit is −0.73 and varies with block count, reaching −0.19 at b = 24 months rather than tracking the window or volatility terciles.Source: §B.11 · pp. 107–108

Panel D, P4 blocked

  • P4’s degradation does not track ĉ: long-short loses 0.269 of 0.716 on the mean row, versus long-only losing 0.052 of 0.194, reflecting held-out-era decay.The experiment identifies Definition 4.7’s decay rather than Theorem 7.4’s optimism, and the two effects do not separate on a published-signal library.Source: §B.11 · p. 107

Panel E, the real-time library

  • In the real-time published library, the selection deficit persists at −0.21 for 1/4, −0.33 for 1/8, and −0.35 for 1/12, while deployed results remain within 0.05.The mean long-short return falls from 0.194 in-sample to 0.148 between sample end and publication and 0.086 afterward, giving multipliers 0.76 and 0.44.Source: §B.11 · p. 108

Panel F, the field’s corrections

  • Across corrections, the long-short winner survives while long-only is marginal: DSR is 1.000 versus z = 2.5, PBO is 0.000 versus 0.356, and SPA is 0.000 versus 0.03–0.05.The haircut agrees in scale and verdict with these corrections, but additionally exposes clock, tail-selection, and ex-ante-search limitations that the stack does not price.Source: §B.11 · p. 108

B.12 Experiment 14: the same five stages, where the answer is known · B.13 The five predictions: power, and what happened · C Notation, and the symbols that are used twice

Experiment 14 shows that the five-stage procedure rejects null and decoy opportunities while opening positions when signal, block length, and coverage conditions permit. The prediction tests provide mixed support: P2 is not refuted where measurable, P1 is largely unsupported, P3’s effective breadth is much smaller than nominal, P4 depends on library design, and P5 remains unconfirmed; the final section consolidates the notation.

B.12 Experiment 14: the same five stages, where the answer is known

  • 0 positions were opened on the null world or any zero-edge decoy, while sensitivity increased with block length and invariant-rule selection reached 94% at four times the declared ceiling.The procedure returned no position in all 1200 null walks at every N; with seventy decoys, it selected the invariant rule in 9.7%, 30%, 71%, and 94% of draws at half, one, two, and four times the ceiling.Source: §B.12 · pp. 109–110
  • The experiment attributes two refusal mechanisms to declaring ρblk = ρ, which drives most refusals at large N, and taking the tail over blocks rather than the declared representation.For the invariant rule, measured dispersion was 0.0066 versus declared 0.10; recomputing neff changed firing rates from 0.7% to 38% and from 0.3% to 99% in the cited cells.Source: §B.12 · pp. 109–110

B.13 The five predictions: power, and what happened

  • P1 was not supported: at Λ = 2 the criteria were indistinguishable, narrow-tail CVaR lost −0.46 and −0.73 on long-short signals, and the predicted advantage did not increase across dispersion terciles.Long-only portfolios showed +0.03 to +0.13 protection, whereas long-short signals showed nothing because they had no tail to protect.Source: §B.13 · pp. 110–111
  • P2 was not refuted where measurable, with fitted slopes of 0.66 ± 0.06 and 1.08 ± 0.12, while selected-rule degradation was 0.83–0.94 of the expected maximum.The υ factor was not testable: equities sat at 0.86 within the admissible box, while bond funds’ 2–3 exceeded its ceiling.Source: §B.13 · p. 111
  • P3’s measured effective breadth was 21.3 versus 133 for long-short signals and 1.6 versus 82 for long-only portfolios, supporting a much smaller complexity factor without testing the ratio itself.The asserted ceiling ratio was 16 against 1.7 across the two libraries, about ten, and 37 under inverse-variance weights.Source: §B.13 · p. 111
  • P4 tracked the plug-in level on the paper’s unfiltered library, but its cross-library ordering was unreadable and published-signal libraries reversed the predicted degradation relationship.The pooled ratios were 1.97 versus 1.82 at Λ = 4 and 2.92 versus 2.82 at Λ = 12; the ordering requires libraries with more than one regime path.Source: §B.13 · pp. 111–112
  • P5 remained unconfirmed because the revealed Kelly fraction requires the worksheet’s shrinkage factor and must be identified more tightly than Experiment 2’s 0.52–0.75 band.Without the shrinkage factor, the prediction is not testable.Source: §B.13 · p. 112

C Notation, and the symbols that are used twice

  • The notation defines the recurrence bound Λ, coherence time ℓ, signal ceiling ρ, regime dispersion ρblk, invariance ratio κ, information measures, and capacity utilisation ϰ, while noting that some symbols are reused by context.The table also specifies that losses use the upper tail whereas experiments use rewards and the lower tail, with both yielding the same c(Λ).Source: C Notation, and the symbols that are… · pp. 113–114

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