Paper deep dive
On the Boundary of Admission Gates: An Injected-Truth Study of Falsification-First Selection in Quantitative Strategy Research
Tianlun Zheng
Intelligence
Status: succeeded | Model: Gemma-4-26B-A4B | Prompt: intel-v1 | Confidence: 92%
Last extracted: 10/13/2026, 4:08:59 AM
Summary
This study evaluates the effectiveness of 'admission gates' (statistical criteria) in quantitative strategy research using an injected-truth protocol with a random-admission control. The research finds that gates effectively eliminate false discoveries in weak-signal regimes (training t < 2.5) but act as pure overhead by reducing adoption rates without adding information when signals are strong. A critical finding is that criteria computed on absolute returns silently reject all candidates, including true signals, due to market volatility inflation; criteria must be evaluated on excess returns. The study also identifies redundant criteria and context-dependent effectiveness based on candidate correlation structures.
Entities (12)
Relation Signals (9)
Absolute Returns → causes → Silent Rejection
confidence 96% · criteria computed on absolute rather than excess returns silently reject every candidate
Excess Returns → enables → Correct Criterion Evaluation
confidence 95% · criteria must be evaluated on excess returns
Admission Gates → reduces → False Discovery Rate
confidence 95% · gates eliminate false discoveries in the weak-signal regime
Admission Gates → iseffectivewhen → Weak Signals
confidence 94% · gates help for training-period t<2.5
Admission Gates → isoverheadwhen → Strong Signals
confidence 94% · add nothing when signals are strong
Admission Gates → reduces → Adoption Rate
confidence 93% · cut adoption to 1–7%
Random-Admission Control → distinguishes → Information from Conservatism
confidence 92% · separating 'carries information' from 'is more conservative'
Deflated Sharpe Ratio → isusedin → Admission Gates
confidence 90% · We use the DSR ... directly as one of our four criteria
Panel III → →
Cypher Suggestions (0)
No Cypher suggestions yet.
Abstract
Abstract:Strategy research conflates two problems: finding a profitable rule, and establishing that the finding is not search luck. The latter calls for admission gates -- statistical criteria that must be satisfied before a conclusion is adopted -- yet whether gates work, and at what cost, remains untested. We introduce an injected-truth protocol with a random-admission control that adopts at the same rate as the gate; only if the gate beats this control does it carry information rather than merely raise a threshold. Across synthetic and real-calibrated panels, gates eliminate false discoveries in the weak-signal regime but cut adoption to 1--7%, and add nothing when signals are strong. Most importantly, criteria computed on absolute rather than excess returns silently reject every candidate, including true signals. Keywords: multiple testing, backtest overfitting, strategy admission, injected-truth validation, excess returns, false discovery rate
Tags
Links
- Source: https://arxiv.org/abs/2610.07701v1
- Canonical: https://arxiv.org/abs/2610.07701v1
Trouble viewing inline? Open PDF directly →
Full Text
29,857 characters extracted from source content.
Expand or collapse full text
On the Boundary of Admission Gates: An Injected-Truth Study of Falsification-First Selection in Quantitative Strategy Research Tianlun Zheng †thanks: Correspondence: simplify23@users.noreply.github.com. Code and data to reproduce every number in this paper are available at https://github.com/simplify23/quant-trading-agent. Affiliation: Fudan University October 2026 Abstract Strategy research conflates two problems: finding a profitable rule, and establishing that the finding is not search luck. The latter calls for admission gates—statistical criteria that must be satisfied before a conclusion is adopted—yet whether gates work, and at what cost, remains untested. We introduce an injected-truth protocol with a random-admission control that adopts at the same rate as the gate; only if the gate beats this control does it carry information rather than merely raise a threshold. Across synthetic and real-calibrated panels, gates eliminate false discoveries in the weak-signal regime but cut adoption to 11–7%7\%, and add nothing when signals are strong. Most importantly, criteria computed on absolute rather than excess returns silently reject every candidate, including true signals. Keywords: multiple testing, backtest overfitting, strategy admission, injected-truth validation, excess returns, false discovery rate 1 Introduction 1.1 Two kinds of failure Data-driven strategy research fails in two qualitatively different ways. Type I failure is not finding: search is inefficient and genuine signals remain undiscovered. Type I failure is finding something false: after searching many candidates on a finite sample, noise is mistaken for signal. The statistical root of Type I failure is elementary—when one tests N strategies and reports the best, the reported statistic is not any single strategy’s performance but an extreme value—but its consequences are not. 1.2 The engineering response, and what it assumes Practitioners and automated research systems respond by inserting admission gates: a set of criteria that a conclusion must satisfy before it is adopted. Current agentic pipelines instantiate this as multi-stage funnels. Wang et al. (2026) report a 92%92\% elimination rate across information-coefficient (IC) screening, correlation filtering, deduplication, and backtesting; Tang et al. (2025) enforce originality, hypothesis–factor alignment, and complexity control; MinervaScore (2026) compose four established validation statistics into a robustness grade. The idea is natural. It is also largely untested, and two pitfalls follow. Conservatism is not effectiveness. Gates usually manifest as adopting less. Without a control one cannot distinguish a gate that carries information from one that simply raised a threshold. A high elimination rate does not settle the question: random elimination at the same rate might do equally well. A gate can fail without announcing it. MinervaScore (2026) calibrate their score on 359,062359,062 production backtests, yet in their pre-registered real-market test it showed no significant forward relationship (Spearman ρs=0.013 _s=0.013, p=0.40p=0.40); the authors describe it as “an auditable validation and reporting layer, rather than evidence of demonstrated real-market predictability.” Having gates is not the same as gates being effective. 1.3 Contributions We ask when admission gates are useful and at what cost, using an injected-truth protocol in which known signals are embedded so that ground truth is observable. Its essential component is a random-admission control that adopts at the same rate as the gate but by coin flip, separating “carries information” from “is more conservative.” Our contributions: 1. A reproducible evaluation protocol for admission gates, including the equal-adoption-rate control (§3.4). 2. An empirical boundary: gates help for training-period t<2.5t<2.5 and are pure overhead beyond it; the cost is quantified in adoption rate and recall (§5). 3. A necessary condition: criteria must be evaluated on excess returns. On absolute returns they systematically and silently reject every candidate, including a ground-truth signal with t=4.0t=4.0 (§5.3). 4. Honest negatives: a redundant sample-size criterion, failed control designs, and a task morphology in which gates are unhelpful (§5.4–5.5). Why it matters. Every automated research pipeline that admits conclusions must decide when to stop believing its own output. Gates are the instrument that decision rests on, yet their effectiveness is typically assumed rather than measured—and the one published calibration of such an instrument reported a null forward result (MinervaScore, 2026). If gates are weaker than assumed, the pipelines that rely on them inherit an unbounded false-discovery risk; if they are merely conservative, those pipelines silently discard real findings. Neither failure is visible from the outside, which is what makes the question worth measuring. We do not claim that gates increase returns, nor that our implementation improves on prior work. 2 Related Work Our paper sits at the intersection of four literatures, and belongs to none of them. We state the branch explicitly in §2.5. 2.1 The replication crisis, quantified in finance Ioannidis (2005) argued that for most study designs the probability that a claimed finding is true is below one half, driven by small samples, small effects, and the number of relationships probed. Finance supplies unusually clean measurements of the same phenomenon. McLean and Pontiff (2016) tracked 97 published cross-sectional predictors and found returns 26%26\% lower out-of-sample and 58%58\% lower post-publication. Harvey et al. (2016) showed that after accounting for the number of factors tried, a newly claimed factor needs t>3.0t>3.0, not 2.02.0. Hou et al. (2020) re-ran 452 published anomalies: 65%65\% fail a single |t|≥1.96|t|≥ 1.96 hurdle, rising to 82%82\% under the multiple-testing hurdle of 2.782.78. This literature establishes that Type I failure is not hypothetical—it is the modal outcome in this field. 2.2 Statistical machinery for data snooping The corrective tools are also mature. Lo and MacKinlay (1990) documented data-snooping bias in asset-pricing tests; Brock et al. (1992) provided the canonical technical-rule study that later work used to quantify snooping; Sullivan et al. (1999) evaluated trading rules by bootstrap against the full universe they were drawn from. White (2000) formalised the Reality Check and Hansen (2005) refined it into the Superior Predictive Ability test. Bailey and López de Prado (2014) introduced the deflated Sharpe ratio, and Bailey et al. (2016) the probability of backtest overfitting; Harvey and Liu (2015) showed the appropriate Sharpe deflation is non-linear in the strategy’s own statistics. We use the DSR (Bailey and López de Prado, 2014) directly as one of our four criteria. 2.3 Robustness scoring and admission in practice A recent line composes these statistics into deployable instruments: MinervaScore (2026) aggregate DSR, PBO, SPA and minimum track record length into a display score; Sheppert (2026) embeds anti-overfitting terms directly into the optimisation objective. Both operate post hoc on a completed backtest. Our question is different in kind: not “how robust is this result?” but “does the rule that decides whether to accept a result actually work, and what does it cost?” The distinction matters because a scoring function’s output is only as useful as the decision rule that consumes it. 2.4 Agentic alpha mining and automated research Automated pipelines attack Type I failure. Xiao et al. (2024) simulate trading-firm organisation with debating analyst agents; Wang et al. (2026) add a memory loop that distils successful and failed mining attempts; Han et al. (2026) evolve whole mining trajectories; Tang et al. (2025) constrain generation by abstract-syntax originality and hypothesis alignment, and have been published at KDD ’25; Kou et al. (2024) combine LLM factor generation with multi-agent evaluation. AlphaSeek (2026) pursue trajectory-level self-iteration. In the broader automated-research literature, Chen et al. (2026) survey 1,250 papers and observe that demonstrated self-improvement tracks a verification hierarchy—formal verifiers >> execution feedback >> learned judges >> intrinsic self-assessment—while Zhao et al. (2026) close the loop on an agent’s own code. Our criteria sit at the execution feedback level of that hierarchy. 2.5 Where this paper sits Table 1: Positioning. This paper belongs to the methodology branch of the replication literature, applied at admission time inside an automated research loop. Replication lit. Robustness scoring Agentic alpha mining This paper Question Are published findings true? How robust is this backtest? How to find more alpha? Are the gates effective, and at what cost? Unit of analysis Published factor One completed backtest Candidate factor A candidate decision When applied Post hoc, after publication Post hoc, before deployment At search time At admission time, inside the loop Output Failure / FDR rates A robustness grade Factors and weights An effectiveness boundary Typical method Surveys, replications Composite statistics LLM agents, evolution Injected truth ++ random-admission control Table 1 states the positioning. Concretely, the paper belongs to the methodology branch of the replication literature (§2.1–2.2): it takes that branch’s diagnosis as given, and instead of measuring how often findings fail, it tests the instrument practitioners built in response. Relative to robustness scoring (§2.3) we change the object of study from a score to a decision rule, and relative to agentic mining (§2.4) our contribution is orthogonal and composable: gates can serve as the admission layer of those pipelines, and a search-efficiency improvement does not by itself make admission more reliable. 3 Method 3.1 Admission decision Let round k propose a candidate ckc_k with evidence EkE_k. The admission decision is (ck,Ek)→vk∈adopt,pending,reject,invalidA(c_k,E_k)→ v_k∈\ adopt, pending, reject, invalid\, where pending denotes not detected (insufficient power) and is strictly distinguished from reject (evidence against). Our experiments use three outcomes: adopt, abstain, and false adoption. 3.2 Criteria We use four criteria (Table 2). Table 2: Admission criteria used in this study. Criterion Definition Analogue G6 sub-period stability Four sub-periods of the training window; at least three have positive mean Parameter plateau F6 leave-one-trade-out After removing the best five trading days, the mean remains positive Single-event-carry check F1 sample size n≥N∗n≥ N^*, N∗=⌈(2σ/μ)2⌉\;N^*= (2σ/μ)^2 Falsification threshold G9a multiple testing Deflated Sharpe ratio ≥0.95≥ 0.95 given Ntrials=40N_trials=40 Trial-count deflation (Bailey and López de Prado, 2014) 3.3 A necessary condition: criteria on excess returns Write strategy j’s return on day t as rjt=wt+εjtr_jt=w_t+ _jt, where wtw_t is the benchmark return and εjt _jt the strategy-specific part. Total volatility is inflated by the market component, σ(rj)≳σ(w)σ(r_j) σ(w), whereas true discernibility depends on α/σ(ε)α/σ( ), not on α/σ(rj)α/σ(r_j). If criteria are evaluated on absolute returns while market volatility dominates—in our panels σ(w)=0.0208σ(w)=0.0208 versus σ(ε)=0.007σ( )=0.007—then the absolute Sharpe of every candidate, including the ground-truth one, lies inside the noise band and all four criteria fail. The correction is to evaluate every criterion on the excess return xjt=rjt−wtx_jt=r_jt-w_t; for the DSR this is the information ratio. We take wtw_t to be the equal-weighted panel return. 3.4 Arms and controls Table 3 lists the four arms. Arm C is the key control: with adoption rates aligned, a criterion carries information if and only if ΔFDR=FDRC−FDRB>0 =FDR_C-FDR_B>0. If ΔFDR≈0 ≈ 0, the gate is merely a stricter threshold. Table 3: Experimental arms. Arm C separates information from conservatism. Arm Rule Purpose A Pure search Adopt the candidate with the highest training-period Sharpe (current practice). B Gate Among candidates passing all four criteria, adopt the highest training Sharpe; abstain if none pass (method under evaluation). C Random admission Adopt arm A’s choice with probability p, otherwise abstain; p tuned so that C’s adoption rate matches B’s (identifies “effective” vs. “merely conservative”). B′ Gate without F1 Arm B with the sample-size criterion removed (ablation). Control design iterations. Our first two designs for arm C were invalid. A Sharpe-quantile threshold always leaves the training-period winner inside the passing set, so “take the best passer” is identical to arm A—confirmed empirically, with identical FDR at every α. “Randomly keep k, then take the best” always adopts for k≥1k≥ 1, so its adoption rate is identically one and cannot be aligned. A valid control must be able to abstain and have a tunable adoption rate. 4 Experimental Setup Real panelInject known α truth observable1 Panel I synthetic Panel I real-calibrated Panel I real cross-section 2 A pure search: highest training Sharpe B gate: adopt best passer, else abstain C random admission: same rate, coin flip 3 compare ΔFDR=FDRC−FDRB =FDR_C-FDR_B 4 Figure 1: The injected-truth protocol, in four numbered steps: (1) inject a known effect so that ground truth becomes observable; (2) instantiate it in one of three panel families; (3) apply three arms to the same candidate set—arm C adopts at the same rate as arm B but by coin flip; (4) compare. Only if ΔFDR>0 >0 does the gate carry information rather than merely being more conservative. Figure 1 summarises the protocol. 4.1 Data and power pre-check We use a panel of 29 A-share ETFs (745 return points, backward-adjusted); Table 4 reports its statistics. Before designing any portfolio-level comparison we compute the smallest detectable effect. A leg with a 30-day minimum holding period yields at most 1010–1313 trades over the 322-day training window, whereas N∗N^* is 9393 trades for μ=1.25%,σ=6%μ=1.25\%,σ=6\% and 576576 for μ=0.5%μ=0.5\%. Portfolio-level comparison is therefore undecidable here—resolving it would require roughly 37 years of data—which is precisely why the injected-truth design is needed (Appendix A lists the reproduction commands). Table 4: Real panel statistics and power pre-check. Panel statistic Value Power item Daily standard deviation 0.020750.02075 Training window: 322 days Kurtosis (normal =3=3) 7.847.84 Trades per leg (upper bound): 10–13 First-order autocorrelation +0.021+0.021 N∗N^* (μ=1.25%μ=1.25\%): 93 trades Mean cross-sectional correlation +0.504+0.504 N∗N^* (μ=0.5%μ=0.5\%): 576 trades 4.2 Panels Panel I (synthetic, independent candidates). T=750T=750 (training 322), N=40N=40 candidates of which K=5K=5 are ground truth. Noise (0,σ2)N(0,σ^2), σ=0.01σ=0.01; ground-truth columns receive a constant α∈0.0004,0.0008,0.0016,0.0032α∈\0.0004,0.0008,0.0016,0.0032\ (annualized 10.1%10.1\%–80.6%80.6\%). 400 repetitions per setting; N∈20,40,80N∈\20,40,80\ for sensitivity. Panel I (real-calibrated strategy family). The benchmark series is the equal-weighted return of the real panel, preserving fat tails and volatility clustering; strategy-specific noise σε∈0.007,0.004 _ ∈\0.007,0.004\ implies inter-strategy correlations of roughly 0.890.89 and 0.960.96. Ground-truth columns receive α calibrated relative to σε _ so that the intended t-statistics are actually attained. Panel I (real cross-section, counter-example). The 29 real ETFs are themselves treated as candidates, i.e. an asset-selection task (§5.5). Metrics: FDR=FDR= share of false among adopted; hit rate == share of runs adopting a ground-truth signal; abstention rate =1−=1- adoption rate. 5 Results and Analysis 5.1 Panel I: help when signals are weak, overhead when they are strong Table 5: Panel I (synthetic, independent candidates), 400 repetitions. α (ann.) train t A FDR B adopt B FDR C FDR Δ Verdict 10.1%10.1\% 0.72 0.5900.590 0.017 0.4000.400 1.000 +0.600+0.600 effective 20.2%20.2\% 1.44 0.2430.243 0.047 0.0000.000 0.200 +0.200+0.200 effective 40.3%40.3\% 2.87 0.010 0.603 0.000 0.010 +0.010+0.010 indistinguishable 80.6%80.6\% 5.74 0.000 1.000 0.000 0.000 +0.000+0.000 indistinguishable 112233445566000.20.20.40.40.60.60.80.811 gate adds nothing beyond here Training-period t of the ground-truth signalFalse discovery rate (FDR)A: pure searchB: gateC: random admission (equal rate) Figure 2: Panel I (400 repetitions). Pure search errs on 24%24\%–59%59\% of weak-signal adoptions; the gate drives FDR to zero but only below t≈2.5t≈ 2.5. To the right of the dotted line the gate is pure overhead: pure search barely errs and gating only lowers the adoption rate (Table 5). Figure 2 plots the same result as a curve: In the weak regime pure search’s FDR is 24%24\%–59%59\%; gates reduce it to zero at the cost of an adoption rate of 1.7%1.7\%–4.7%4.7\%. For training t>2.5t>2.5, pure search already errs essentially never (FDR ≤1%≤ 1\%) and gates add no value while lowering the adoption rate. 5.2 Panel I: stable across data source and correlation structure Table 6: Panel I (real-calibrated strategy family), 400 repetitions each. σε _ (corr.) t A FDR B adopt B FDR B hit B abstain 0.007 (≈0.89≈ 0.89) 1.00 0.3880.388 0.012 0.0000.000 0.013 0.988 0.007 1.51 0.1880.188 0.073 0.0340.034 0.070 0.927 0.007 2.51 0.020 0.387 0.0000.000 0.388 0.613 0.007 4.00 0.003 0.982 0.0000.000 0.983 0.018 0.004 (≈0.96≈ 0.96) 0.99 0.4150.415 0.017 0.0000.000 0.018 0.983 0.004 1.53 0.1820.182 0.068 0.0000.000 0.068 0.932 0.004 2.51 0.018 0.395 0.0000.000 0.395 0.605 0.004 3.99 0.000 0.987 0.0000.000 0.988 0.013 Table 6 reports both correlation levels. The real-calibrated panel reproduces the morphology of the synthetic one: in the weak regime arm A’s FDR is 18%18\%–42%42\% while arm B’s is ≈0≈ 0, with abstention of 93%93\%–99%99\%. The conclusion is therefore not an artifact of the i.i.d. assumption. Holding t=1.44t=1.44 fixed, Δ for N∈20,40,80N∈\20,40,80\ is +0.250+0.250, +0.200+0.200, +0.317+0.317—all positive, so neither candidate count nor ground-truth share changes the direction of the result. 5.3 Diagnostic experiment: the excess-return requirement Before the correction of Section 3.3, arm B abstained 100%100\% of the time even at t=4.0t=4.0. Figure 3 and Table 7 give per-criterion rejection rates for ground-truth columns and identifies the cause: under absolute returns the market component dominates total volatility and compresses the effective t-statistic by roughly a factor of three, so the DSR never passes. After the correction, arm B at t=4.0t=4.0 attains a hit rate of 98.3%98.3\% while keeping FDR at zero. G6F6F1G9a000.50.511CriterionRejection rate on ground-truth columnst=1.00t=1.00t=2.51t=2.51t=4.00t=4.00 Figure 3: Per-criterion rejection rate on ground-truth columns before the excess-return correction. The DSR rejects a true signal 100%100\% of the time at every strength: under absolute returns the market component inflates volatility and compresses the effective t-statistic by roughly a factor of three. Table 7: Per-criterion rejection rate for ground-truth columns (pre-correction), Panel I. Criterion t=1.00t=1.00 t=2.51t=2.51 t=4.00t=4.00 G6 sub-period stability 1.00 0.60 0.40 F6 leave-one-trade-out 1.00 0.60 0.20 F1 sample size (N∗N^*) 1.00 1.00 0.80 G9a DSR 1.001.00 1.001.00 1.001.00 Finding (central). The failure is silent: it presents as “the framework found nothing,” easily misread as “the candidates are poor.” Any gate framework should define criteria on excess returns and, at deployment, print per-criterion rejection rates for ground-truth versus noise columns. 5.4 Ablation: the sample-size criterion is redundant Across the three Panel I settings, arm B′ and arm B produce bit-identical results: the N∗N^* criterion is fully covered by the DSR in this regime. This does not establish that N∗N^* is useless—when trials are few and single-run sample size binds, it may still be necessary—but it is reported as a negative ablation result. 5.5 Task morphology matters Treating the 29 real ETFs as candidates (Panel I), arm A attains a 100%100\% hit rate and FDR =0=0 at every signal strength, while gates only cause missed opportunities. The cause is the 0.5040.504 mean cross-sectional correlation: assets receiving injected α systematically outperform the rest, so the training-period winner is necessarily a ground-truth signal. An injected-truth protocol must match the candidate structure of the task under study, or one may wrongly conclude that gates are harmful. 6 Discussion 6.1 What gates are for Our results position admission gates as a precision device, not a return device. Use them when the candidate count is large, the training window is limited, and the cost of a wrong adoption exceeds the cost of a miss—for example when capital is at stake. Do not use them when the signal is already strong (training t>2.5t>2.5), where they only reduce the adoption rate. The result resonates with the replication literature. Ioannidis (2005) notes that a finding is less likely to be true when effect sizes are small and many relationships are probed—the regime in which our gates help. Conversely Harvey et al. (2016) and Hou et al. (2020) document that failures concentrate in exactly the marginal cases our gates reject. Gates are therefore best understood as implementing, at decision time, the multiple-testing discipline this literature prescribes after the fact. 6.2 Relation to prior work Section 2 positions this paper; two points bear emphasis here. First, relative to robustness scoring (MinervaScore, 2026; Sheppert, 2026) we change the object of study from a score to a decision rule, and the excess-return requirement (§3.3) applies to those scores as much as to ours. Second, relative to agentic mining (Wang et al., 2026; Han et al., 2026; Tang et al., 2025; Kou et al., 2024; AlphaSeek, 2026) our contribution is composable: gates can serve as their admission layer, and improved search efficiency does not by itself make admission more reliable. 6.3 Limitations 1. Synthetic component. Ground truth is injected as a constant effect; real alpha decay and regime dependence are more complex. Panel I uses real return series as the common factor—preserving kurtosis 7.847.84 and cross-correlation 0.5040.504—and reproduces the synthetic morphology, which mitigates but does not eliminate the concern. 2. Single market, single asset class (A-share ETFs, 29 assets / 745 points). 3. Incomplete criterion set. Difference-trade auditing, selection degree-of-freedom diagnostics, and PBO/SPA are implemented in the framework but not exercised here. 4. Thresholds are not calibrated. The DSR level of 0.950.95 and the 2σ/μ2σ/μ coefficient follow prior choices; their sensitivity is not scanned. 5. Abstention has no utility model. Abstention is recorded as “not adopted” without an explicit trade-off between the cost of a miss and the cost of a wrong adoption. 6.4 Future work Introduce an explicit utility function to ground thresholds in decision theory; extend the protocol to PBO/SPA and difference-trade auditing to map criterion redundancy; repeat across markets and asset classes; and apply it to audit the admission stages of published methods. 7 Conclusion We tested whether admission gates in quantitative research are effective, using an injected-truth protocol on synthetic independent candidates and on strategy-family panels calibrated to a real ETF panel. Gates carry genuine information—at equal adoption rates their false discovery rate is well below that of random admission (Δ 0.100.10–0.600.60), so they are not merely a stricter threshold. But the value has a boundary: it materialises only for training t<2.5t<2.5, at the cost of an adoption rate of 1%1\%–7%7\%; beyond t≈2.5t≈ 2.5 pure search suffices and gating is pure overhead. Criteria must be defined on excess returns, or they silently reject all candidates. A sample-size criterion proved redundant here, and in an asset-selection morphology the gates were unhelpful. In one sentence: admission gates increase decisional precision at a substantial cost in recall. Treating them as return enhancers is a category error; treating them as a conservative decision device under uncertainty—and validating, with the control protocol above, that they beat random admission at the same adoption rate—is their correct role. Appendix A Reproducibility Every number in this paper is reproducible from the accompanying artefacts: python3 exp1_injected_gate_efficacy.py --reps 400python3 exp1_injected_gate_efficacy.py --reps 300 \ --n-cand 20 --k-true 5 --alphas 0.0008python3 exp2_real_based_validation.py --reps 400 \ --panel-kind strategy --sigma-e 0.007 \ --alphas 0.00039 0.00059 0.00098 0.00156python3 exp2_real_based_validation.py --reps 400 \ --panel-kind strategy --sigma-e 0.004 \ --alphas 0.00022 0.00034 0.00056 0.00089python3 exp2_real_based_validation.py --reps 300 \ --panel-kind asset \ --alphas 0.00116 0.00174 0.00289 0.00463 Data anchor: etf_panel_ts.frozen-20260930.json (29 ETFs, 746 days, backward-adjusted). Results are written to *_results.json. References Brock et al. (1992) W. Brock, J. Lakonishok, and B. LeBaron. Simple technical trading rules and the stochastic properties of stock returns. The Journal of Finance, 47(5):1731–1764, 1992. Bailey and López de Prado (2014) D. H. Bailey and M. López de Prado. The deflated Sharpe ratio: Correcting for selection bias, backtest overfitting, and non-normality. The Journal of Portfolio Management, 40(5):94–107, 2014. DOI: 10.3905/jpm.2014.40.5.094. Bailey et al. (2016) D. H. Bailey, J. M. Borwein, M. López de Prado, and Q. J. Zhu. The probability of backtest overfitting. Journal of Computational Finance, 20(4), 2016. Hansen (2005) P. R. Hansen. A test for superior predictive ability. Journal of Business & Economic Statistics, 23(4):365–380, 2005. Harvey and Liu (2015) C. R. Harvey and Y. Liu. Backtesting. The Journal of Portfolio Management, 42(1), 2015. (Page ranges in secondary sources differ, 12–28 versus 13–28; verify against the publisher record.) Harvey et al. (2016) C. R. Harvey, Y. Liu, and H. Zhu. … and the cross-section of expected returns. The Review of Financial Studies, 29(1):5–68, 2016. DOI: 10.1093/rfs/hhv059. Hou et al. (2020) K. Hou, C. Xue, and L. Zhang. Replicating anomalies. The Review of Financial Studies, 33(5):2019–2133, 2020. DOI: 10.1093/rfs/hhy131. Ioannidis (2005) J. P. A. Ioannidis. Why most published research findings are false. PLoS Medicine, 2(8):e124, 2005. DOI: 10.1371/journal.pmed.0020124. Lo and MacKinlay (1990) A. W. Lo and A. C. MacKinlay. Data-snooping biases in tests of financial asset pricing models. The Review of Financial Studies, 3(3):431–467, 1990. McLean and Pontiff (2016) R. D. McLean and J. Pontiff. Does academic research destroy stock return predictability? The Journal of Finance, 71(1):5–32, 2016. DOI: 10.1111/jofi.12365. Sullivan et al. (1999) R. Sullivan, A. Timmermann, and H. White. Data-snooping, technical trading rule performance, and the bootstrap. The Journal of Finance, 54(5):1647–1691, 1999. DOI: 10.1111/0022-1082.00163. White (2000) H. White. A reality check for data snooping. Econometrica, 68(5):1097–1126, 2000. Tang et al. (2025) Z. Tang, Z. Chen, J. Yang, J. Mai, Y. Zheng, K. Wang, J. Chen, and L. Lin. AlphaAgent: LLM-driven alpha mining with regularized exploration to counteract alpha decay. In Proc. 31st ACM SIGKDD Conf. (KDD ’25), V.2, Toronto, Canada, August 2025. arXiv:2502.16789; DOI: 10.1145/3711896.3736838. Xiao et al. (2024) Y. Xiao, E. Sun, D. Luo, and W. Wang. TradingAgents: Multi-agents LLM financial trading framework. arXiv preprint arXiv:2412.20138, 2024. Wang et al. (2026) FactorMiner: A memory-augmented, self-evolving agent for alpha factor mining. arXiv preprint arXiv:2602.14670, 2026. Han et al. (2026) J. Han, S. Zhang, W. Li, and et al. QuantaAlpha: An evolutionary framework for LLM-driven alpha mining. arXiv preprint arXiv:2602.07085, 2026. Kou et al. (2024) Z. Kou, H. Yu, J. Luo, and et al. Automate strategy finding with LLM in quant investment. arXiv preprint arXiv:2409.06289, 2024. MinervaScore (2026) Equity strategy backtesting: Luck or edge? The MinervaScore as a statistical robustness grade. arXiv preprint arXiv:2608.23808, 2026. Sheppert (2026) A. P. Sheppert. The GT-Score: A robust objective function for reducing overfitting in data-driven trading strategies. arXiv preprint arXiv:2602.00080, 2026. Chen et al. (2026) M. Chen, L. Wang, and B. Qu. Recursive self-improvement in AI: From bounded self-refinement to autonomous research loops. arXiv preprint arXiv:2607.07663, 2026. Zhao et al. (2026) B. Zhao, Z. Jiang, Y. Wu, D. Srikanth, and D. Xu. Recursive self-improvement of AI research agents. arXiv preprint arXiv:2609.26457, 2026. AlphaSeek (2026) AlphaSeek: Trajectory-level self-iterative factor mining framework for multi-source financial data. arXiv preprint arXiv:2608.13913, 2026.