Two-Draw Clause-Union U-Statistics, Task-Routing Bounds, Synthetic Specification-Grader Mismatches, and Latent Reasoning Replay in LLM Agent Harnesses

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Abstract

Different single-model harnesses for GPT-6 Luna on Harness-Bench—such as Rust Codex 0.166.0 (persistent JS REPL, apply_patch, and 100% /v1/responses encrypted reasoning replay at 6.48 mUSD/episode) and Python Nanobot Batch-Index (Mode 50, Turn-0 workspace index, 89% batch reads, and 0% replay at 3.00 mUSD/episode)—achieve similar task means (~65%) at 2.16x different solver cost. We study how their clause-level failures relate and what controlled interventions change across 1,450 unique archived episodes (70 runs; 0.00 USD new spend), 160 synthetic model-organism episodes (MO-Suite; 0.2501 USD), and 60 counterbalanced Harness-Bench development episodes (Experiment W; 0.1703 USD). First, using two-sample Hoeffding U-statistics, we derive an exact signed sample identity decomposing unity into single-draw mean, within-package two-draw gain, unbiased excess cross-package two-draw union ($\widehat{\Delta}_{\text{div}}$, removing +5.14 pp upward plug-in bias under the null at $n_A=2, n_B=5$), and two-draw joint failure ($\widehat{C}_{AB}$). Across 50 tasks (241 clauses), Codex-versus-Mode-50 $\widehat{\Delta}_{\text{div}}$ is $+0.33$ pp (95% CI $[-2.27, +2.93]$) to $+0.79$ pp ($[-1.02, +2.59]$), versus $7.73$ pp within-package two-draw gain and $27.81\%$ joint failure. Because $\Delta_{\text{div}}$ is quadratic in $(p_A - p_B)$ whereas task routing scales linearly with $|\mu_{t,A} - \mu_{t,B}|$, small $\widehat{\Delta}_{\text{div}}$ does not exclude task specialization: 2-fold cross-fitted per-task routing gains $+2.81$ points ($[+0.09, +5.53]$) over the 50/50 package mean ($+3.09$ points $[-0.94, +7.12]$ over Mode 50). Second, across eight paired synthetic tasks, Mode 50 scores 100.0% (35/35) when specifications and graders align, whereas unquoting three reason strings in MO-4b drops vocabulary pass rate from 95% to 0% ($p = 3.05 \times 10^{-10}$) with concentrated naming (51%–100% coincidence), and live Turn-2 pre-receipt re-grading shows 0/30 post-receipt score changes in Mode 55. Finally, enabling reasoning replay on Mode 50 yields $-0.20$ points ($[-5.97, +5.57]$, $1.0153\times$ complete cost), supporting our $+3.50$-point stopping gate.

Two-Draw Clause-Union U-Statistics, Task-Routing Bounds, Synthetic Specification-Grader Mismatches, and Latent Reasoning Replay in LLM Agent Harnesses

1. Problem, Scope, and Contributions

Across published studies on Harness-Bench [1, 4–8] and parallel community evaluations (Posts 30–32 [19, 20]), distinct single-model harnesses driving gpt-6-luna reach similar aggregate task means despite large differences in interface architecture, tool syntax, latent state replay, and token expenditure. On the 40-task exposure-qualified validation split, Released Codex 0.166.0 (a Rust harness using a persistent JavaScript REPL, apply_patch mutations, 100% pre-mutation shell execution, and 100% /v1/responses reasoning.encrypted_content replay at 6.482 mUSD solver cost/episode) averages 65.67%, whereas Batch-Index (Nanobot Mode 50 [5], a Python harness using a Turn-0 workspace index, a 19-word batch-read reminder, write_file/edit_file/apply_patch tools, 26.3% pre-mutation exec, and 0% reasoning replay at 3.000 mUSD/episode) averages 65.19%. Meanwhile, post-draft executable self-repair (ESWV-Lean [6], ESWV-Risk [8]) and turn-collapsing policies [7] have encountered tight cost–quality tradeoffs.

Three analytical and experimental questions motivate this study:

  1. Separating two-draw clause-union diversity from finite-sample binomial noise and linear task routing: Scalar task means can mask opposing clause-level differences, while within-package 2-trial unions (agent_harness_1 v3 [4]) estimate $p_{t,c}^{(H)}(1 - p_{t,c}^{(H)})$ rather than cross-package divergence $(p_{t,c}^{(A)} - p_{t,c}^{(B)})^2$ [9, 10]. Conversely, naive plug-in estimates $\frac{1}{2}(\hat{p}_A - \hat{p}_B)^2$ across small replicate counts ($n_A = 2$ vs. $n_B = 5$) suffer $+5.14$ percentage points of upward sampling-variance bias under the exact null $p_A \equiv p_B$. At the same time, quadratic excess two-draw union and linear per-task routing estimate distinct policy quantities and must not be conflated.
  2. Isolating specification–grader representation mismatches and post-write AST receipts under controlled synthetic semantics: Prior benchmark error audits (agent_harness_1 v3 Section 4.6 & Table A3 [4]) showed that persistent Harness-Bench check failures mix unspecified output conventions with substantive algorithmic errors. Controlled synthetic workspaces with known reference solutions and paired negative controls allow us to measure what happens when a specification omits exact grader strings—and to audit before/after draft checkpoints when a harness appends post-write static AST receipts.
  3. Single-factor isolation of /v1/responses latent reasoning replay on a lean substrate: Codex 0.166.0 replays reasoning.encrypted_content on 100% of follow-up turns (1,939 reasoning tokens/episode on validation), whereas Nanobot Mode 50 drops encrypted reasoning items (837 reasoning tokens/episode). Testing replay as a single factor on Mode 50 measures its direct score, clause-union, and token-substitution effects on that substrate.

We investigate these three questions across 1,450 unique archived episodes (70 unique runs; 1,700 cohort-run evaluations at 0.00 USD new spend), 160 live synthetic model-organism episodes (0.2501 USD; plus a 0.0049 USD 2-episode pre-flight check), and 60 prospective counterbalanced Harness-Bench development episodes (0.1703 USD):

  1. Signed Two-Sample U-Statistic Decomposition and Cross-Fitted Task-Routing Bounds (Section 3, 70 unique runs): Using Hoeffding U-statistics [11], we derive an exact signed finite-sample identity decomposing unity into Single-Draw Mean ($\widehat{\bar{\mu}}$), Within-Package Two-Draw Gain ($\widehat{\bar{V}}_{\text{within}}$), Unbiased Excess Cross-Package Two-Draw Clause Union ($\widehat{\Delta}_{\text{div}} = \widehat{U}_{AB} - \frac{1}{2}(\widehat{U}_{AA} + \widehat{U}_{BB})$, unbiased for $\frac{1}{2}(p_A - p_B)^2$), and Two-Draw Joint Failure Rate ($\widehat{C}_{AB} = 1 - \widehat{U}_{AB}$). Across all 50 tasks (241 positive-weight clauses), Codex vs. Mode 50 excess two-draw union is +0.33 pp (95% task-cluster CI $[-2.27, +2.93]\text{ pp}$ on concurrent S9 2v2) to +0.79 pp (95% CI $[-1.02, +2.59]\text{ pp}$ on 2v8), compared with 7.73 pp within-package two-draw gain and 27.81% two-draw joint failure. We prove and empirically verify that because $\Delta_{\text{div}}$ is quadratic in $(p_A - p_B)$ whereas oracle task routing scales linearly with $|\mu_{t,A} - \mu_{t,B}| \le \sqrt{D_{\text{task}}}$, small $\widehat{\Delta}_{\text{div}}$ does not rule out task-level specialization: the Cauchy–Schwarz 95% upper confidence limit on oracle task routing over $\bar{\mu}$ is 9.84 pp (2v8), and 2-fold out-of-sample cross-fitted per-task routing gains +2.81 points (95% CI $[+0.09, +5.53]$) over $\bar{\mu}$ and +3.09 points ([-0.94, +7.12]) over Mode 50 alone (at Codex's 2.16x solver cost on routed tasks).
  2. Synthetic Model Organisms (MO-Suite) and Pre-Receipt Turn-2 Trajectory Audit (Section 4, 160 episodes): Across eight paired positive/negative control tasks (telemetry_gate.py, cooler_ledger.py, bench_events.db + inspect_bench_log, and canary_planner.py), frozen Mode 50 and Mode 54-Wire both score 100.00% (35 / 35 episodes) on the seven tasks whose specifications and seed workspaces align with the grader (MO-1a..MO-4a). Replacing three quoted rejection reason strings in MO-4b ("burn_ceiling", "sample_floor", "skew_limit") with "a concise snake_case reason" while keeping the exact-string grader fixed drops vocabulary pass rate from 19 / 20 (95.0%) to 0 / 20 (0.0%, two-sided Fisher $p = 3.05 \times 10^{-10}$), with concentrated naming on that task (20/20 "cohort_skew", 19/20 "insufficient_samples", 14/20 "burn_rate_breach"). Reconstructing and live-grading all 120 pre-receipt Turn-2 Python drafts alongside all 160 final deliverables (280 grade_w1() executions) shows 119 / 120 identical Turn-2 and final scores: all 7 / 7 soak_windows reset ValueError guards on MO-4a/4b (5 in Mode 55, 1 in Mode 50, 1 in Mode 54) were written in Turn 2 prior to any receipt under ambiguous validation wording in docs/rollout_contract.md (5/10 vs. 9/10 direct Mode 55 vs. Mode 50, two-sided Fisher $p = 0.1409$; 5/10 vs. 28/30 pooled non-frame, $p = 0.0062$), and Mode 55's post-write AST receipt changed 0 / 30 Python episode scores (0 / 5 soak_windows guards removed; 8 / 10 MO-4 episodes making zero-gain math.isfinite micro-edits).
  3. Prospective Counterbalanced Replay Evaluation on Mode 50 (Experiment W, Section 5, 60 episodes): Isolating /v1/responses reasoning.encrypted_content replay on Mode 50 (Mode 54-Wire, 30/30 multi-turn episode replay vs. 0/30 in Mode 50) across three counterbalanced AB, BA, AB development blocks yields -0.20 points (95% CI $[-5.97, +5.57]$, exact $2^{10}$ sign-flip $p = 1.0000$; 0.00 points across Python tasks 080, 150, 154; $3\text{v}3$ $\widehat{\Delta}_{\text{div}} = -1.52\text{ pp}$) at 1.0153x complete official cost. Fresh reasoning output tokens shift by -113.8 tokens/episode (-13.5%, 95% CI $[-336.1, +108.5]$), concentrated on Turns $\ge 2$ (-118.2 $[-339.5, +103.1]$ vs. Turn 1 +4.4 $[-1.4, +10.2]$) and offset by +3,507 (+6.6%) replayed input tokens. Missing our pre-registered +3.50-point advancement gate supports stopping Mode 54-Wire on Mode 50 without claiming statistical equivalence or attributing Codex's reasoning volume.

Scope and Methodological Qualifications

  • Observational cross-package contrasts vs. controlled interventions: Released Codex 0.166.0 and Nanobot Mode 50 differ simultaneously across language runtime, tool schemas, context indexing, shell patterns, and wire replay; Section 3 estimates net cross-package properties across those full packages, whereas controlled intervention claims are restricted to MO-Suite (Section 4, noting Mode 55's two-part bundle in Section 4.1) and Experiment W (Section 5, scoped to Mode 50).
  • Strict validation and grader firewall: Zero hidden benchmark grader files (tests/, design.md, task.yaml) were opened in any split, and zero validation task prompts or workspaces were opened (firewall_audit: 0 reads across all 70 archived runs). All validation records in data/archival_raw_clause_matrix.json anonymize task and check identifiers to val_DDD and clause_DD and remain exposure-qualified given prior validation evaluations of Codex and Modes 47–53 [5, 6, 8].
  • Model and pricing scope: All measurements evaluate gpt-6-luna (temperature = 1.0) under official prices.json rates (0.10 / 0.01 / 0.125 / 0.50 USD per $10^6$ uncached / cached / cache-write / output tokens).

2. Related Work

Coincident failure models, U-statistics, and binomial bounds. Multiversion software-reliability theory shows that independent implementations exhibit positive failure correlation whenever input difficulty varies across tasks (Eckhardt & Lee [9]) or distinct designs encounter shared specification ambiguities (Littlewood & Miller [10]). Estimating quadratic cross-package divergence $(p_A - p_B)^2$ without upward small-sample binomial bias requires two-sample Hoeffding U-statistics [11], while zero-pass finite-sample support requires exact Clopper–Pearson confidence limits [18]. In LLM reasoning and code generation, majority voting (Self-Consistency, Wang et al. [12]) and same-model verification (agent_harness_1 v3 [4]) improve performance only when errors disperse around a correct mode; notably, [4] (Section 4.6, Table A3) already documented pair unions, coincident failures, and the coexistence of unspecified output conventions with substantive semantic errors on Harness-Bench development tasks 018, 080, and 154.

Intrinsic self-correction, static feedback, and agent-computer interfaces. Prior studies show that ungrounded self-critique frequently fails to repair initial reasoning errors or induces spurious edits (Huang et al. [13]; Kamoi et al. [14]), while executable self-repair depends critically on feedback fidelity and cost (Olausson et al. [15]). On SWE-bench and Harness-Bench [1–3], interface ergonomics (SWE-agent, Yang et al. [16]; Complexity Trap, Lindenbauer et al. [17]; Batch-Index [5]; output-token substitution in agent_harness_4 v3 [7]) and candidate-blind executable screening (ESWV-Lean [6]; ESWV-Risk [8]; Posts 30, 32 [19, 20]) define our lean Nanobot Mode 50 baseline. We extend this literature by separating quadratic two-draw clause union from linear cross-fitted task routing across packages, testing deliberate specification–grader string mismatches and pre/post-receipt Turn-2 drafts in MO-Suite, and isolating /v1/responses reasoning replay on Mode 50.


3. Two-Draw Clause-Union U-Statistics, Task-Routing Bounds, and Archival Audit

3.1 Signed Two-Sample U-Statistic Identity, Routing Bounds, and Exchangeability

Consider $T$ tasks where positive-weight non-gate clause $c$ on task $t$ carries normalized benchmark weight $\tilde{w}_{t,c} = \frac{w_{t,c}}{T \sum_{c'} w_{t,c'}}$ ($\sum_{t,c} \tilde{w}_{t,c} = 1$) and effective pass probabilities $p_{t,c}^{(A)}, p_{t,c}^{(B)} \in [0, 1]$ (requiring all task gates to pass) under harness packages $A$ and $B$. For a single clause (suppressing $(t,c)$ before taking the $\tilde{w}_{t,c}$-weighted sum), let $U_{AA} = 2p_A - p_A^2$ and $U_{BB} = 2p_B - p_B^2$ denote within-package two-draw union pass probabilities, and let $U_{AB} = p_A + p_B - p_A p_B$ denote the cross-package two-draw union pass probability (passing in at least one of one independent draw from $A$ and one from $B$). The population excess cross-package two-draw clause union is

$$ \Delta_{\text{div}}(A, B) \;:=\; U_{AB} - \frac{1}{2}\big(U_{AA} + U_{BB}\big) \;=\; \frac{1}{2}(p_A - p_B)^2 \;\ge\; 0, $$

yielding the population identity

$$ 1 \;\equiv\; \underbrace{\frac{p_A + p_B}{2}}_{\bar{\mu}\text{ (Single-Draw Mean)}} \;+\; \underbrace{\frac{p_A(1 - p_A) + p_B(1 - p_B)}{2}}_{\bar{V}_{\text{within}}\text{ (Within-Package 2-Draw Gain)}} \;+\; \underbrace{\frac{(p_A - p_B)^2}{2}}_{\Delta_{\text{div}}\text{ (Excess 2-Draw Union)}} \;+\; \underbrace{(1 - p_A)(1 - p_B)}_{C_{AB}\text{ (Two-Draw Joint Failure)}}. $$

Here $C_{AB} = 1 - U_{AB}$ is strictly the probability that one draw from $A$ and one independent draw from $B$ both miss the clause; it is not an irreducible failure floor under $k > 2$ draws or modified policies.

Signed finite-sample U-statistics. Given $n_A \ge 2$ and $n_B \ge 2$ independent runs $Y_{1}^{(A)}, \dots, Y_{n_A}^{(A)} \sim \text{Bern}(p_A)$ and $Y_{1}^{(B)}, \dots, Y_{n_B}^{(B)} \sim \text{Bern}(p_B)$, the distinct-pair Hoeffding U-statistics [11]

$$ \widehat{U}_{AA} = \frac{2}{n_A(n_A - 1)}\sum_{1 \le i < j \le n_A} \max\!\big(Y_i^{(A)}, Y_j^{(A)}\big), \quad \widehat{U}_{BB} = \frac{2}{n_B(n_B - 1)}\sum_{1 \le i < j \le n_B} \max\!\big(Y_i^{(B)}, Y_j^{(B)}\big), \quad \widehat{U}_{AB} = \frac{1}{n_A n_B}\sum_{i=1}^{n_A}\sum_{k=1}^{n_B} \max\!\big(Y_i^{(A)}, Y_k^{(B)}\big) $$

define unbiased estimators $\widehat{\bar{\mu}} = \frac{1}{2}(\hat{p}_A + \hat{p}_B)$, $\widehat{\bar{V}}_{\text{within}} = \frac{1}{2}(\widehat{U}_{AA} - \hat{p}_A + \widehat{U}_{BB} - \hat{p}_B)$, $\widehat{\Delta}_{\text{div}} = \widehat{U}_{AB} - \frac{1}{2}(\widehat{U}_{AA} + \widehat{U}_{BB})$, and $\widehat{C}_{AB} = 1 - \widehat{U}_{AB}$ satisfying $\widehat{\bar{\mu}} + \widehat{\bar{V}}_{\text{within}} + \widehat{\Delta}_{\text{div}} + \widehat{C}_{AB} = 1$ on every sample. Crucially, $\widehat{\Delta}_{\text{div}}$ is signed in finite samples: for $n_A = n_B = 2$ with one pass in each arm, $\widehat{\bar{\mu}} = 0.50$, $\widehat{\bar{V}}_{\text{within}} = 0.50$, $\widehat{\Delta}_{\text{div}} = -0.25$, and $\widehat{C}_{AB} = 0.25$. The sample equation is thus a signed estimator identity, not a partition into nonnegative single-draw shares. By contrast, naive plug-in $\frac{1}{2}(\hat{p}_A - \hat{p}_B)^2$ has strictly positive null bias $+\frac{1}{2}p(1-p)\big(\frac{1}{n_A} + \frac{1}{n_B}\big)$: across $5{,}000$ Monte Carlo trials ($50$ clauses, $n_A = 2, n_B = 5$, $p_{t,c} \sim \text{Beta}(0.8, 0.8)$), plug-in averages +5.14 pp under $H_0: p_A = p_B$, whereas $\widehat{\Delta}_{\text{div}}$ averages +0.04 pp under $H_0$ and recovers +3.26 pp (true: $+3.20\text{ pp}$) under opposing $\pm 40\text{ pp}$ clause shifts.

Why $\Delta_{\text{div}}$ does not bound task routing. Let $\mu_{t,H} = \sum_c \frac{w_{t,c}}{\sum_{c'} w_{t,c'}} p_{t,c}^{(H)}$ denote package $H$'s expected score on task $t$. An oracle per-task router selects the higher-expectation package on each task, gaining

$$ \Delta_{\text{route}}^{\star} \;:=\; \frac{1}{T}\sum_{t=1}^{T} \max(\mu_{t,A}, \mu_{t,B}) - \bar{\mu} \;=\; \frac{1}{2T}\sum_{t=1}^{T} |\mu_{t,A} - \mu_{t,B}| $$

over the 50/50 package average $\bar{\mu}$ (and $\Delta_{\text{route}}^{\star} + \frac{1}{2}(\mu_A - \mu_B)$ over package $B$ alone). Because $\Delta_{\text{div}}$ is quadratic in $(p_A - p_B)$ whereas $\Delta_{\text{route}}^{\star}$ is linear in $|\mu_{t,A} - \mu_{t,B}|$, a small $\Delta_{\text{div}}$ can coexist with substantial routing gains: for two single-clause tasks with $(p_A, p_B) = (0.55, 0.45)$ and $(0.45, 0.55)$, $\Delta_{\text{div}} = 0.005$ ($0.5\text{ pp}$) yet $\Delta_{\text{route}}^{\star} = 0.05$ ($5.0\text{ pp}$). By Cauchy–Schwarz and Jensen's inequality,

$$ \Delta_{\text{route}}^{\star} \;\le\; \sqrt{D_{\text{task}}} \;\le\; \sqrt{\tfrac{1}{2}\Delta_{\text{div}}}, \qquad \text{where } D_{\text{task}} := \frac{1}{4T}\sum_{t=1}^{T}(\mu_{t,A} - \mu_{t,B})^2. $$

We estimate $D_{\text{task}}$ unbiasedly via the task-score U-statistic $\widehat{D}_{\text{task},t} = \frac{1}{4}\big(\widehat{U}_{AA,t}^{(\text{sq})} + \widehat{U}_{BB,t}^{(\text{sq})} - 2\hat{\mu}_{t,A}\hat{\mu}_{t,B}\big)$ (where $\widehat{U}_{HH,t}^{(\text{sq})}$ averages $S_{t,i}^{(H)} S_{t,j}^{(H)}$ over distinct pairs), report $\sqrt{\max(0, \text{UCL}_{95}(D_{\text{task}}))}$ as an upper confidence bound on $\Delta_{\text{route}}^{\star}$, and directly evaluate 2-fold out-of-sample cross-fitted task routing (selecting the higher-mean package per task on fold 1 with ties defaulting to cheaper Mode 50, evaluating on fold 2, and averaging with the reverse fold).

Uncertainty and permutation exchangeability. Because clauses within a task episode are correlated, our primary confidence intervals for $\Delta_{\text{div}}$, $\mu_A - \mu_B$, $D_{\text{task}}$, and cross-fitted routing treat the $T$ task-level estimates as independent clusters using Student-$t_{T-1}$ intervals (requiring only independence across tasks/runs, without assuming equal within-task clause correlation across packages). Supplementary permutation $p$-values test stronger distributional nulls: whole-run permutations ($p_{\text{run}}$) assume run-level vectors across all tasks are exchangeable across cohorts (strictly satisfied under homogeneous concurrent scheduling, and an approximation across pooled historical cohorts), while task-stratified episode permutations ($p_{\text{strat}}$) assume identical within-task multi-clause joint distributions $F_{t,A} = F_{t,B}$ (stronger than equality of clause marginals $p_{t,c}^{(A)} = p_{t,c}^{(B)}$ alone).

3.2 Archival Cross-Package Decomposition and Routing Results (70 Unique Runs)

Evaluating 70 unique archived runs (45 development runs = 450 unique episodes; 25 exposure-qualified validation runs = 1,000 unique episodes; 1,450 unique episodes on disk, referenced 1,700 times across cohort definitions because concurrent S9 runs also belong to full All cohorts) shows strong behavioral divergence alongside small two-draw union excess (Tables 1–2, Figure 1).

Table 1. Behavioral and wire-telemetry separation across single-pass cohorts (36 unique development runs + 22 unique exposure-qualified validation runs; validation telemetry means shown).

| Harness Package Cohort | Dev Ep (Score) | Val Ep (Score) | Val Solver (mUSD/ep) | Turn-1 Batch Read | Turn-2 Immed. Write | Pre-Write exec | Val Reas. Tokens/Ep | Wire encrypted_content Replay | | :--- | :---: | :---: | :---: | :---: | :---: | :---: | :---: | :---: | | Released Codex 0.166.0 | 20 (57.05%) | 80 (65.67%) | 6.482 | 0.0% | 2.5% | 100.0% | 1,939.0 | 100.0% | | Stock Nanobot (Mode 1) | 70 (55.10%) | 80 (63.85%) | 4.670 | 0.0% | 8.8% | 32.5% | 1,013.6 | 0.0% | | C-Clean (Mode 47 [5]) | 20 (55.85%) | 80 (67.01%) | 3.349 | 7.5% | 25.0% | 40.0% | 904.1 | 0.0% | | Index-Clean (Mode 49 [5]) | 40 (54.25%) | 160 (62.92%) | 3.233 | 15.6% | 46.8% | 32.5% | 868.2 | 0.0% | | Batch-Index (Mode 50 [5]) | 170 (55.27%) | 320 (65.19%) | 3.000 | 89.3% | 75.2% | 26.3% | 837.4 | 0.0% | | Batch-Index-Med (Mode 51) | 20 (53.20%) | 80 (66.56%) | 3.245 | 89.9% | 74.7% | 27.9% | 870.5 | 0.0% |

Table 2. Signed two-draw U-statistic decompositions, task-cluster 95% CIs, Cauchy–Schwarz oracle routing 95% UCLs, and 2-fold cross-fitted task-routing gains across splits ($\widehat{\bar{\mu}} + \widehat{\bar{V}}_{\text{within}} + \widehat{\Delta}_{\text{div}} + \widehat{C}_{AB} = 100.00\%$).

| Package Pair ($A$ vs. $B$, Runs $n_A \text{v} n_B$) | Split (T / Clauses) | $\mu_A - \mu_B$ (95% CI) | $\widehat{\bar{V}}_{\text{within}}$ / $\widehat{C}_{AB}$ | Biased Plug-In | Signed $\widehat{\Delta}_{\text{div}}$ (95% CI) | Route $\text{UCL}_{95}$ ($\sqrt{D_{\text{task}}}$) | 2-Fold Cross-Fit Route $-\,\bar{\mu}$ (95% CI) | $p_{\text{run}}$ / $p_{\text{strat}}$ | | :--- | :---: | :---: | :---: | :---: | :---: | :---: | :---: | :---: | | Mode 50 Split-Half (8v9 Ctrl) | Dev (10/50) | +1.80 | 6.96% / 37.63% | +0.91 pp | +0.08 pp | — | — | 0.374 / 0.327 | | Codex vs. Mode 50 (S9, 2v2) | Dev (10/50) | -1.65 ([-10.19, +6.89]) | 8.62% / 34.15% | +3.66 pp | -0.65 pp ([-5.98, +4.68]) | 7.61 pp | -0.43 pp ([-7.19, +6.34]) | 1.000 / 0.534 | | Codex vs. Mode 50 (All, 2v17) | Dev (10/50) | +1.78 ([-5.81, +9.37]) | 7.69% / 36.10% | +2.37 pp | +0.05 pp ([-2.54, +2.65]) | 5.98 pp | -2.70 pp ([-8.64, +3.25]) | 0.421 / 0.447 | | Codex vs. Mode 50 (S9, 2v2) | Val (40/191) | +2.24 ([-5.28, +9.76]) | 8.53% / 26.34% | +4.84 pp | +0.58 pp ([-2.50, +3.65]) | 12.50 pp | +3.31 pp ([-0.57, +7.18]) | 0.667 / 0.326 | | Codex vs. Mode 50 (All, 2v8) | Val (40/191) | +0.48 ([-5.84, +6.80]) | 7.57% / 25.93% | +3.52 pp | +1.07 pp ([-1.13, +3.26]) | 11.21 pp | +4.32 pp ([+1.32, +7.31]) | 0.089 / 0.060 | | Mode 50 Split-Half (4v4 Ctrl) | All (50/241) | +1.85 | 7.30% / 29.22% | +1.91 pp | +0.08 pp | — | — | 0.457 / 0.390 | | Codex vs. Mode 50 (S9, 2v2) | All (50/241) | +1.46 ([-4.69, +7.61]) | 8.55% / 27.90% | +4.61 pp | +0.33 pp ([-2.27, +2.93]) | 10.80 pp | +2.56 pp ([-0.75, +5.87]) | 0.667 / 0.384 | | Codex vs. Mode 50 (All, 2v8) | All (50/241) | +0.55 ([-4.63, +5.73]) | 7.73% / 27.81% | +3.27 pp | +0.79 pp ([-1.02, +2.59]) | 9.84 pp | +2.81 pp ([+0.09, +5.53]) | 0.111 / 0.093 | | Codex vs. Stock (2v2) | All (50/241) | +1.81 | 7.49% / 29.66% | +3.55 pp | -0.19 pp | — | — | 0.667 / 0.561 | | Mode 49 vs. Mode 50 (4v8) | All (50/241) | -2.21 | 7.52% / 30.08% | +1.53 pp | +0.11 pp | — | — | 0.364 / 0.346 |

Figure 1: (a) Signed 4-part two-draw U-statistic decomposition across archival pairs (50 tasks, 241 clauses). (b) Contrast between biased plug-in quadratic gap, unbiased two-draw excess union (with 95% task-cluster CIs), and linear 2-fold cross-fitted per-task routing gain over the 50/50 package mean.

3.3 Empirical Interpretation: Two-Draw Ensembling vs. Task Routing and Zero-Pass Support

  1. Removing plug-in bias shrinks excess two-draw clause union, while preserving room for modest task-level specialization: On development, naive plug-in suggests $+3.66\text{ pp}$ (S9) / $+2.37\text{ pp}$ (2v17) excess union, whereas unbiased $\widehat{\Delta}_{\text{div}}$ is -0.65 pp (95% CI $[-5.98, +4.68]$) and +0.05 pp ($[-2.54, +2.65]$); moreover, Codex's development advantage on core: True clauses ($+5.47\text{ pp}$) vs. core: False clauses ($-13.00\text{ pp}$) reverses sign on validation ($-0.72\text{ pp}$ vs. $+5.28\text{ pp}$). Across all 50 tasks (2v8), $\widehat{\Delta}_{\text{div}} = +0.79\text{ pp}$ (SE = 0.90 pp, 95% CI $[-1.02, +2.59]\text{ pp}$), indicating that blindly running one Codex draw and one Mode 50 draw adds at most ~2.6 pp (95% upper limit) over within-package two-draw union (7.73 pp). By contrast, linear 2-fold cross-fitted per-task routing gains +4.32 points (95% CI $[+1.32, +7.31]$) over $\bar{\mu}$ on validation (+2.81 points $[+0.09, +5.53]$ across all 50 tasks, or +3.09 points $[-0.94, +7.12]$ relative to Mode 50 alone; Cauchy–Schwarz 95% UCL 9.84 pp), though achieving such gains prospectively would require predicting per-task package affinity without oracle history while paying Codex's 2.16x solver cost on routed tasks.
  2. Observed zero-pass clause support and Clopper–Pearson bounds: Across all 36 archived single-pass development runs (extended to 42 single-pass runs including Experiment W), 9 / 50 clauses (21.50% of development weight) have 0 / 42 observed passes (exact Clopper–Pearson [18] two-sided 95% CI [0.00%, 8.41%], one-sided 95% UCL 6.88%). Across all 22 archived single-pass validation runs, 29 / 191 clauses (16.50% of validation weight) have 0 / 22 observed passes (two-sided 95% CI [0.00%, 15.44%], one-sided 95% UCL 12.73%). Zero observed passes bound rather than prove zero underlying pass probability, and as [4] (Section 4.6, Table A3) demonstrated on development tasks 018, 080, and 154, persistent check failures often combine unquoted output conventions with substantive semantic or algorithmic errors (Appendix B.2).

4. Synthetic Model Organisms (MO-Suite) and Pre-Receipt Turn-2 Audit

4.1 Reconciled Paired Tasks (mo_suite.py) and Evaluated Container Arms

To study specific failure mechanisms and screen candidate interventions without touching Harness-Bench, we built MO-Suite (model_organisms/mo_suite.py), a zero-contamination suite of eight deterministic tasks in four positive/negative control pairs, verified by 11 / 11 reference and adversarial calibration assertions in model_organisms/test_mo_calibration.py:

  • Pair 1 (MO-1a Frame Inheritance vs. MO-1b Explicit Contract Override — Satellite Downlink Packet Gatekeeper): Repairs evaluate_packet(packet, state) in src/telemetry_gate.py (docs/downlink_spec.md), implementing 16-bit checksum validation (compute_crc16), sequence-window gap buffering and contiguous drain, atomic epoch rollover, caller state immutability, and seven verdict_code strings ("accepted_frame", "crc_mismatch", "epoch_regressed", "duplicate_seq", "gap_buffered", "gap_overflow", "malformed_header"). In MO-1a, five of the seven codes are defined only in $W_0$ (src/telemetry_gate.py); a scratch rewrite inventing replacement names ("bad_crc", "window_full") scores 0.65. Counter-organism MO-1b explicitly renames 'crc_mismatch' -> 'integrity_fault' and 'gap_overflow' -> 'window_exceeded' in docs/downlink_spec.md; a blind $W_0$-literal shield retaining the legacy codes scores 0.65.
  • Pair 2 (MO-2a Admissible Domain vs. MO-2b Contracted Rejection — Cold-Chain Vaccine Cooler Audit): Implements audit_readings(readings) in src/cooler_ledger.py (docs/cooler_contract.md) over unit_id, elapsed_min, door_count, excursion_streak, audit_seq, and temp_c ([2.0, 8.0]), forbidding re/IO/clock imports. MO-2a admits any non-empty trimmed printable ASCII unit_id and allows excursion_streak to reset to 0 on temperature recovery (an over-constrained mock inventing CLR-DDD slug or excursion_streak monotonicity ValueError guards scores 0.45). MO-2b explicitly requires CLR-DDD formatting and strict audit_seq monotonicity (a permissive mock stripping ValueError rejections scores 0.55).
  • Pair 3 (MO-3a Binary SQLite Ledger vs. MO-3b Static CSV — Centrifuge Calibration Reconciliation): Reconciles data/rotors.csv (RTR-01..RTR-06) under docs/calibration_sop.md into output/schedule.json and output/HANDOFF.md. MO-3a stores unmerged cycle batches, resets, and fault locks (RUN_BATCH, BENCH_RESET, VIBRATION_LOCK, SEAL_BREACH) in binary SQLite state/bench_events.db, inspectable via executable bin/inspect_bench_log (a CSV-only synthesis ignoring SQLite scores 0.00). MO-3b has no database (unmerged_bench_cycles = 0), measuring static-task overhead.
  • Pair 4 (MO-4a Quoted Reason Tokens vs. MO-4b Deliberate Spec–Grader String Mismatch — Canary Rollout Planner): Both tasks share identical seed code (src/canary_planner.py), inputs, 8-rule rollout precedence, and exact-match graders (grade_w1 weights: 0.45 algorithmic_precedence_and_monotonicity, 0.40 exact_reason_vocabulary_closure, 0.15 pure_boundary). In MO-4a, docs/rollout_contract.md explicitly quotes all nine reason literals ("telemetry_lag", "slo_breach", "burn_ceiling", "initial_cohort", "sample_floor", "skew_limit", "soak_incomplete", "step_advance", "rollout_complete"). In MO-4b, the three newly added rejection rules (burn_ceiling, sample_floor, skew_limit) replace the quoted token with "a concise snake_case reason" while the grader still requires the MO-4a strings (0.60 maximum when only exact_reason_vocabulary_closure fails).

We evaluated four rootless-Docker container arms (5 replicates $\times$ 8 tasks = 40 episodes/arm, 160 episodes, physical spend 0.250081 USD; Appendix B.1):

  1. mode50_ctrl (NANOBOT_SCPC_MODE=50): Frozen Batch-Index baseline (0% wire reasoning replay, no post-write AST receipts).
  2. mode54_wire (NANOBOT_SCPC_MODE=54): Single-factor /v1/responses reasoning.encrypted_content replay (100% multi-turn episode replay; identical prompt, index, and tools to Mode 50).
  3. mode56_blindshield (NANOBOT_SCPC_MODE=56): Negative-control arm appending [W0 Literal Shield WARNING] whenever any $W_0$ string literal is removed from a .py file.
  4. mode55_frame (NANOBOT_SCPC_MODE=55): Two-part static representation bundle (sada_lean_runtime.py lines 1094, 1149, 1559–1687) combining (a) Turn-0 workspace-index annotations on .sqlite/.db files ("binary DB — inspect via exec") and extensionless scripts ("executable CLI script")—active on MO-3a, inactive on MO-1, MO-2, MO-4 where Turn-0/Turn-1 inputs are byte-identical to Mode 50—and (b) a post-write [AST Frame & Precondition Diff] receipt listing imports, unmentioned $W_0$ literal removals, and AST ValueError preconditions.

4.2 MO-Suite Results and Live Pre-Receipt Turn-2 Trajectory Audit (280 grade_w1 Runs)

Table 3. Complete 160-episode MO-Suite evaluation (5 replicates/cell; 40 episodes/arm; official gpt-6-luna pricing).

| Harness Container Arm | All 8 Orgs (n=40) | Aligned 7 Orgs (MO-1a..4a, n=35) | MO-4a Quoted (n=5) | MO-4b Unquoted (n=5) | MO-1b Override (Reas. Tok / mUSD) | MO-3b Static (mUSD/ep) | Mean Cost (mUSD/ep) | Wire Replay Ep Rate | Screening Gate | | :--- | :---: | :---: | :---: | :---: | :---: | :---: | :---: | :---: | :--- | | mode50_ctrl (Mode 50) | 93.88% | 100.00% (35/35) | 100.0% | 51.0% | 839.8 / 2.15 | 0.644 | 1.538 | 0.0% | Baseline | | mode54_wire (Replay) | 93.88% | 100.00% (35/35) | 100.0% | 51.0% | 584.0 / 1.53 | 0.908 (+41%) | 1.591 (1.03x) | 100.0% | PASS $\to$ Exp W | | mode56_blindshield | 95.00% | 100.00% (35/35) | 100.0% | 60.0% | 1,267.2 (+51%) / 2.57 | 0.578 | 1.508 | 0.0% | FAIL (MO-1b tax) | | mode55_frame (Bundle) | 87.75% | 96.86% (33/35) | 83.0% | 24.0% | 815.0 / 1.98 | 0.626 | 1.615 (1.05x) | 0.0% | STOPPED |

Figure 2: (a) MO-Suite 160-episode scores across aligned organisms (MO-1a..MO-4a), quoted MO-4a, and unquoted MO-4b. (b) Concentrated naming choices across n=20 MO-4b episodes under deliberate specification-grader string mismatch.

  1. 100% baseline accuracy on self-consistent synthetic tasks (MO-1a..MO-4a): Both mode50_ctrl and mode54_wire scored 100.00% (35 / 35 episodes) across Pairs 1–3 and MO-4a, using edit_file on 100% (15/15) of surgical bug-repair episodes (MO-1a, MO-1b, MO-4a) and exec on 100% (5/5) of binary SQLite episodes (MO-3a) without needing Mode 55's index hints. On MO-1b, mode56_blindshield inflated reasoning tokens by $+50.9\%$ (839.8 $\to$ 1,267.2) while reconciling false $W_0$ warnings against explicit contract overrides.
  2. Deliberate specification–grader string mismatch on MO-4b: Replacing three quoted reason strings with "a concise snake_case reason" reduced exact_reason_vocabulary_closure pass rate from 15 / 15 (100% non-frame; 19 / 20 overall) on MO-4a to 0 / 20 (0%) on MO-4b (two-sided Fisher exact $p = 3.05 \times 10^{-10}$ overall; $p = 1.29 \times 10^{-8}$ non-frame). Live execution of all $n = 20$ delivered MO-4b modules (Table 4) shows strongly concentrated naming on this task ("cohort_skew" 20/20, "insufficient_samples" 19/20, "burn_rate_breach" 14/20, yielding 50.0% exact 3-tuple pairwise coincidence and 0.0% grader string match)—illustrating how outputs can satisfy visible prose instructions while failing an unquoted exact-match check in every arm.

Table 4. Concentrated naming distributions across all $n = 20$ MO-4b delivered modules (4 arms $\times$ 5 replicates; live-verified in Tier 2).

| Unquoted Rejection Branch (MO-4b) | Grader String (MO-4a) | Observed gpt-6-luna Strings ($n = 20$) | Pairwise Coincidence | Grader Match | | :--- | :--- | :--- | :---: | :---: | | skew_case (cohort_skew_bps > max_skew_bps) | "skew_limit" | "cohort_skew": 20 / 20 (100%) | 100.00% | 0.00% | | sample_case (sample_size < min_samples) | "sample_floor" | "insufficient_samples": 19 / 20 (95%), "sample_volume": 1 / 20 | 90.00% | 0.00% | | burn_case (burn_rate > max_burn_rate) | "burn_ceiling" | "burn_rate_breach": 14 / 20 (70%), "error_budget_breach": 3, "error_budget_burn": 3 | 51.05% | 0.00% | | Joint 3-Tuple (burn, sample, skew) | ("burn_ceiling", "sample_floor", "skew_limit") | ("burn_rate_breach", "insufficient_samples", "cohort_skew"): 14 / 20 (70%) | 50.00% | 0.00% |

  1. Pre-receipt Turn-2 re-grading refutes second-pass guard invention and exposes static-receipt inertness (Mode 55): On MO-4a/4b (where Mode 55's Turn-0 index changes are inactive), algorithmic_precedence_and_monotonicity passed in 5 / 10 (50%) mode55_frame episodes versus 9 / 10 (90%) in mode50_ctrl (direct two-sided Fisher $p = 0.1409$) and 28 / 30 (93.3%) across pooled non-frame arms (two-sided Fisher $p = 0.0062$). All seven 0.15-scoring episodes (5 mode55_frame, 1 mode50_ctrl, 1 mode54_wire) failed because they raised ValueError when traffic_pct changed without soak_windows == 0. To test whether Mode 55's post-write receipt induced those guards, we reconstructed every initial Turn-2 Python module (w_turn2, written before any receipt was emitted) from transactions.json across all 120 Python episodes (data/mo_suite_episodes_160.json) and ran live grade_w1():
    • Pre-receipt origin under specification ambiguity: docs/rollout_contract.md placed the sentence "soak_windows resets after traffic changes and may decrease freely" inside Section "## 1. Structural & Continuity Validation (ValueError)", permitting a plausible validation interpretation. All 7 / 7 soak_windows reset ValueError guards (and mode55_frame's 0.75 draft on MO-1a r5) were already present in Turn 2 (w_turn2) before any post-write receipt was shown, so the 5/10 vs. 9/10 gap ($p = 0.1409$) reflects pre-receipt Turn-2 construction variation rather than receipt-induced invention.
    • Post-receipt trajectory behavior (0 / 30 score changes at 1.39x MO-4 cost): Across all 120 Python episodes, score(w_turn2) differed from score(w_final) in only 1 / 120 episodes (mode50_ctrl__MO-1b__r3: 0.75 -> 1.00), and in 0 / 30 mode55_frame episodes. Even though Mode 55's emitted receipt explicitly listed "pct != previous['traffic_pct'] and snap['soak_windows'] != 0" alongside "remove any uncontracted guard that rejects valid inputs", 0 / 5 Mode 55 episodes removed that guard; instead, 8 / 10 Mode 55 MO-4a/4b episodes spent an extra mutation-and-test cycle adding isinstance(burn_rate, float) before math.isfinite(burn_rate), raising MO-4 cost by 1.39x (2.08 vs. 1.50 mUSD/ep in Mode 50) without changing a single score.

5. Prospective Single-Factor Evaluation of Latent Reasoning Replay (Experiment W)

Because only Mode 54-Wire passed MO-Suite's accuracy screen, Experiment W (manifests/understanding_m3_wire_dev_manifest.json) evaluated frozen Mode 54-Wire (NANOBOT_SCPC_MODE=54) against concurrent frozen Mode 50 (ctrl50, NANOBOT_SCPC_MODE=50) across three counterbalanced AB, BA, AB blocks on development (6 runs, 60/60 scored episodes, 456/456 solver and 12/12 semantic-judge requests usage-complete, 0 errors; physical spend 0.170307 USD; Table 5, Figure 3, and Appendix A).

Table 5. Prospective single-factor Experiment W on development ($N = 10, \text{df} = 9$; 30 episodes/arm across counterbalanced AB, BA, AB blocks; task-paired 95% Student-$t$ CIs).

| Metric / Estimand | ctrl50 (Batch-Index Mode 50) | mode54_wire (Mode 50 + encrypted_content Replay) | Task-Paired Difference / Ratio (Mode 54-Wire minus Mode 50) | | :--- | :---: | :---: | :---: | | Scored Episodes / Wire Replay Ep Rate | 30 / 30 / 0.0% (0/30) | 30 / 30 / 100.0% (30/30) | Exact single-factor wire separation | | Mean Outcome Score (Full Credit) | 52.13% (5 / 30) | 51.93% (3 / 30) | -0.20 pts, 95% CI [-5.97, +5.57], sign-flip $p = 1.0000$ (4W/4T/2L) | | Python Code-Repair Mean (080, 150, 154) | 33.33% (9 ep) | 33.33% (9 ep) | 0.00 pts (0 / 15 clauses changed 3-run pass rate) | | Data & Document Mean (7 tasks) | 60.19% (21 ep) | 59.90% (21 ep) | -0.29 pts | | Mean Requests (Turns) / Episode | 7.73 (232 total) | 7.47 (224 total) | -0.27 req/ep, 95% CI [-1.50, +0.96] (-3.4%) | | Mean Input Tokens / Ep (Uncached) | 53,145.7 (6,647.6) | 56,652.8 (7,436.8) | +3,507.1 tok/ep, 95% CI [-8,182, +15,196] (+6.6%) | | Turn-1 Fresh Reasoning Tokens / Ep | 2.3 | 6.7 | +4.4 tok/ep, 95% CI [-1.4, +10.2] | | Turns $\ge 2$ Fresh Reasoning Tokens / Ep | 840.1 | 722.0 | -118.2 tok/ep, 95% CI [-339.5, +103.1] (-14.1%) | | Total Fresh Reasoning (All Output) / Ep | 842.4 (3,222.1) | 728.6 (3,091.5) | -113.8 tok/ep, 95% CI [-336.1, +108.5] (-13.5% reas., -4.1% out) | | Official Solver Cost (mUSD/ep) | 0.082223 USD (2.741) | 0.083448 USD (2.782) | +0.041 mUSD/ep, 95% CI [-0.365, +0.446] (1.0149x) | | Complete Official Cost (mUSD/ep) | 0.084506 USD (2.817) | 0.085801 USD (2.860) | 1.0153x complete cost (<= 1.20x gate met) | | 3v3 Signed Excess 2-Draw Union $\widehat{\Delta}_{\text{div}}$ | $\widehat{U}_{BB} = 61.60\%$ | $\widehat{U}_{AA} = 59.57\%$ | $-1.52\text{ pp}$ ($\widehat{U}_{AB} = 59.07\%$, exact $\binom{6}{3}=20$ perm $p = 1.0000$) | | Observed 0%-Pass Dev Clauses (9 clauses) | 0 / 9 passed (0.0%) | 0 / 9 passed (0.0%) | 0 / 42 single-pass runs (95% Clopper–Pearson CI [0.00%, 8.41%]) |

Figure 3: (a) Counterbalanced Experiment W (60 development episodes) comparing Mode 54-Wire against concurrent Mode 50 (ctrl50): -0.20 points (95% CI -5.97 to +5.57) at 1.0153x complete cost. (b) Per-task score deltas across all 10 development tasks and 3v3 signed two-draw U-statistic (-1.52 pp).

Experiment W establishes two bounded conclusions on Batch-Index (Mode 50):

  1. Stopping decision on Mode 50 without equivalence overclaiming: Enabling reasoning.encrypted_content replay across 30/30 multi-turn episodes produced -0.20 points (95% CI $[-5.97, +5.57]$, $p = 1.0000$), 0.00 points difference across Python tasks 080, 150, 154 (0 / 15 clause pass-rate changes), 0 / 9 movement on the archival zero-pass development clauses, and $3\text{v}3$ $\widehat{\Delta}_{\text{div}} = -1.52\text{ pp}$ ($\widehat{C}_{AB} = 40.93\%$, $\widehat{\bar{V}}_{\text{within}} = 8.55\%$). Because $[-5.97, +5.57]$ allows both meaningful gains and losses—including our pre-registered +3.50-point advancement threshold—this estimate justifies our stopping decision not to promote Mode 54-Wire, rather than proving accuracy equivalence.
  2. Substrate-scoped token substitution: On Mode 50, Turn 1 dispatches an immediate batch read_file with virtually zero reasoning (2.3 vs. 6.7 tokens); on Turns $\ge 2$, replaying encrypted items shifted fresh reasoning output by -118.2 tokens/episode (95% CI $[-339.5, +103.1]$) while adding +3,507.1 input tokens (+6.6%), yielding 1.0153x complete cost (mirroring the flat-cost channel substitution pattern in [7] and concurrent native-Nanobot replay observations on r/agent_harness). Because Experiment W varies replay only inside Mode 50, it does not isolate replay's effect inside Codex 0.166.0 or identify sequential exec/JS-REPL calls as the causal source of Codex's 1,939 reasoning tokens/episode; testing that hypothesis requires a controlled intervention on Codex itself.

6. Discussion and Offline Reproducibility

6.1 Summary of Methodological and Empirical Contributions

  1. Distinguishing quadratic two-draw union from linear task routing: Two-sample Hoeffding U-statistics eliminate substantial upward plug-in bias (+3.27 to +4.84 pp on Codex vs. Mode 50) and show that blind one-draw-per-package clausewise ensembling adds little over within-package rerolling (+0.79 pp, 95% CI [-1.02, +2.59], vs. 7.73 pp). At the same time, Cauchy–Schwarz bounds (9.84 pp 95% UCL) and 2-fold cross-fitted per-task routing (+2.81 pts [+0.09, +5.53] over $\bar{\mu}$) show why small quadratic union divergence should never be misread as a sub-1-point ceiling on task-specific routing.
  2. Value of pre-treatment draft auditing in synthetic mechanism studies: In MO-Suite, Mode 50 solved 35 / 35 aligned episodes while MO-4b isolated how unquoted exact-match grader strings induce concentrated 0%-pass naming (50% 3-tuple coincidence). Crucially, retaining and live-grading pre-receipt Turn-2 drafts (w_turn2) overturned a plausible post-hoc "receipt-induced over-constraint" narrative, proving that ambiguous specification placement in docs/rollout_contract.md caused Turn-2 guard variation before any receipt appeared, while Mode 55's post-write static AST receipt failed to repair 5 / 5 false-rejecting guards despite listing them directly.
  3. Bounded replay economics on Batch-Index: Experiment W closes single-factor /v1/responses reasoning replay on Mode 50 (-0.20 pts [-5.97, +5.57], 1.0153x complete cost) without validation expenditure.

6.2 Four-Tier Raw-Record Reproducibility (verify_understanding_paper_stats.py)

Running python3 -B analysis/verify_understanding_paper_stats.py inside an unpacked supplement.zip ($< 3$ seconds, Python 3 standard library only; 42 files, 1,918,758 B expanded $< 2.0$ MB) executes four raw-record verification tiers:

  • Tier 1 (Archival Raw-Matrix Reconstruction): Recomputes U-statistics, task-level SEs, 2-fold cross-fitted routing, task-stratified permutations, Clopper–Pearson zero-pass bounds, and the 5,000-trial Monte Carlo calibration directly from the 1,450 raw anonymized episode clause vectors in data/archival_raw_clause_matrix.json (0 firewall reads).
  • Tier 2 (Live MO-Suite Re-Grading of Final & Turn-2 Deliverables): Executes model_organisms/test_mo_calibration.py (11/11 controls) and runs mo_suite.grade_w1() live across all 160 final deliverables plus all 120 reconstructed pre-receipt Turn-2 Python drafts (280 live runs), verifying 0 / 30 post-receipt score changes in Mode 55, Fisher $p$-values (0.1409, 0.0062, $3.05 \times 10^{-10}$), and live plan_canary_rollout() 3-tuples across all 20 MO-4b modules.
  • Tier 3 (Experiment W Raw-Record Reconstruction): Recomputes token costs from prices.json, task-paired score and Turn-1 / Turns $\ge 2$ reasoning CIs, 0 / 9 zero-pass clause movement, and the 3v3 clause U-statistic (-1.52 pp, exact $\binom{6}{3}=20$ permutation $p = 1.0000$) from data/experiment_w_60_episodes_raw.json and results/.
  • Tier 4 (Pure-Python Source Patch Reconstruction & SHA-256 Digest Verification): Applies code/mode50_to_modes54_55_56.patch to code/mode50_base/ in pure Python, verifies exact SHA-256 matches on all 7 frozen target files in manifests/understanding_m3_wire_dev_manifest.json, dynamically imports the reconstructed sada_lean_runtime.py to verify 30 live AST receipts byte-for-byte, and checks secret-free hygiene. Tiers 1 & 3 reconstruct estimators from retained records, Tier 2 & 4 execute retained code and verify cryptographic source digests, while live gpt-6-luna API generation requires live credentials and benchmark containers.

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Appendix A. Per-Task Development Breakdown and Execution Ledgers (Experiment W & MO-Suite)

Table A1. Per-task Experiment W (development, 3 replicates/arm) score breakdown (ctrl50 vs. mode54_wire).

| Development Task ID | Modality | ctrl50 Reps (r1, r2, r3) | ctrl50 Mean | mode54_wire Reps (r1, r2, r3) | mode54_wire Mean | Paired $\Delta$ (pts) | | :--- | :---: | :---: | :---: | :---: | :---: | :---: | | 008-db-doc-consistency | Data/Doc | 55.0, 45.0, 55.0 | 51.67% | 45.0, 90.0, 55.0 | 63.33% | +11.67 | | 015-email-thread-merge | Data/Doc | 65.0, 40.0, 65.0 | 56.67% | 65.0, 65.0, 55.0 | 61.67% | +5.00 | | 018-cross-doc-citation-check | Data/Doc | 45.0, 45.0, 45.0 | 45.00% | 45.0, 45.0, 45.0 | 45.00% | +0.00 | | 029-multitable-join-analysis | Data/Doc | 100.0, 100.0, 41.0 | 80.33% | 41.0, 75.0, 75.0 | 63.67% | -16.67 | | 031-accessibility-conformance-sample-repair | Data/Doc | 100.0, 100.0, 80.0 | 93.33% | 100.0, 100.0, 100.0 | 100.00% | +6.67 | | 062-privacy-dsar-intake-review | Data/Doc | 100.0, 63.0, 0.0 | 54.33% | 75.0, 25.0, 67.0 | 55.67% | +1.33 | | 066-async-ops-window-rollup | Async/Ops | 40.0, 30.0, 50.0 | 40.00% | 30.0, 30.0, 30.0 | 30.00% | -10.00 | | 080-multipart-artifact-resume-recovery | Python | 5.0, 0.0, 5.0 | 3.33% | 5.0, 5.0, 0.0 | 3.33% | +0.00 | | 150-webauthn-counter-risk-repair | Python | 45.0, 25.0, 25.0 | 31.67% | 45.0, 25.0, 25.0 | 31.67% | +0.00 | | 154-postgres-expand-contract-migration-repair | Python | 60.0, 75.0, 60.0 | 65.00% | 60.0, 75.0, 60.0 | 65.00% | +0.00 |

Table A2. Complete Experiment W counterbalanced AB, BA, AB execution ledger (2026-11-15 UTC; 60/60 scored episodes) and MO-Suite spend reconciliation.

| Run / Study Name | Arm / Scope | UTC Start–Finish | Wall (s) | Scored | Mean Score | FC | Solver Reqs (Known) | Input / Output Tok | Solver USD | Complete USD | | :--- | :---: | :---: | :---: | :---: | :---: | :---: | :---: | :---: | :---: | :---: | | und-m3-wire-ctrl50-dev-r1 | ctrl50 | 04:43:43–04:46:58 | 194 | 10/10 | 61.50% | 3 | 74 (74) | 511,796 / 30,500 | 0.025061 | 0.025801 | | und-m3-wire-mode54_wire-dev-r1 | mode54_wire | 04:46:58–04:50:08 | 189 | 10/10 | 51.10% | 1 | 75 (75) | 568,397 / 31,490 | 0.028037 | 0.028875 | | und-m3-wire-mode54_wire-dev-r2 | mode54_wire | 04:50:08–04:53:19 | 191 | 10/10 | 53.50% | 1 | 73 (73) | 526,566 / 29,503 | 0.025925 | 0.026688 | | und-m3-wire-ctrl50-dev-r2 | ctrl50 | 04:53:19–04:56:33 | 194 | 10/10 | 52.30% | 2 | 69 (69) | 461,770 / 29,822 | 0.024673 | 0.025426 | | und-m3-wire-ctrl50-dev-r3 | ctrl50 | 04:56:33–05:00:56 | 262 | 10/10 | 42.60% | 0 | 89 (89) | 620,805 / 36,340 | 0.032489 | 0.033278 | | und-m3-wire-mode54_wire-dev-r3 | mode54_wire | 05:00:56–05:05:10 | 253 | 10/10 | 51.20% | 1 | 76 (76) | 604,620 / 31,753 | 0.029487 | 0.030238 | | MO-Suite Smoke + Pairs 1–3 + Pair 4 | 4 Arms (162 ep) | 04:10–04:36 | 980 | 162/162 | 92.72%* | 140* | 830 (830) | Deterministic (0 judge) | 0.254934 | 0.254934 |

*MO-Suite primary study comprises 160 episodes (0.172431 USD on Pairs 1–3 + 0.077650 USD on Pair 4 = 0.250081 USD, 92.63% grand mean across all 4 arms $\times$ 8 organisms, 138/160 full-credit) plus a 2-episode pre-flight wire smoke check (0.004852 USD); total new official API spend across the entire study is 0.425240 USD.


Appendix B. Container Implementation Digests and Observed Zero-Pass Clause Support

B.1 Container Specifications and Source Digests (code/mode50_base/ + code/mode50_to_modes54_55_56.patch)

All container arms branch from Batch-Index (Mode 50 [5], harness-starters/gemini1-nanobot:eswv-risk-ctrl50, sha256:3daa4f8da2d1...). Applying code/mode50_to_modes54_55_56.patch to code/mode50_base/ reconstructs all seven frozen files verified against manifests/understanding_m3_wire_dev_manifest.json:

  • Mode 54-Wire (NANOBOT_SCPC_MODE=54, sha256:88f7721f5495..., single-factor replay): Captures reasoning items (id, summary, encrypted_content) in openai_responses/parsing.py, retains "reasoning_items" in openai_compat_provider.py:_ALLOWED_MSG_KEYS, runner.py, and utils/helpers.py, and replays them into input in openai_responses/converters.py strictly when NANOBOT_SCPC_MODE == "54". Zero prompt, index, tool, or receipt changes relative to Mode 50.
  • Mode 55-Frame (NANOBOT_SCPC_MODE=55, sha256:9ed503f8901c..., two-part bundle evaluated only on MO-Suite): Keeps replay_reasoning == False (0% wire replay) and changes two components in sada_lean_runtime.py: (1) Turn-0 build_w0_batch_index tags .sqlite/.db files as "binary DB — inspect via exec" (line 1094) and extensionless executable/#! files as "executable CLI script" (line 1149), which fire on MO-3a (state/bench_events.db, bin/inspect_bench_log) and are inactive on MO-1, MO-2, MO-4; and (2) maybe_append_frame_diff_receipt (lines 1559–1687) appends [AST Frame & Precondition Diff] after .py mutations (write_file, edit_file, apply_patch), listing non-typing imports, unmentioned $W_0$ string removals, and AST raise ValueError conditions.
  • Mode 56-BlindShield (NANOBOT_SCPC_MODE=56, sha256:f2a36f84e6b5..., negative-control stress arm): Keeps Turn-0 indexing identical to Mode 50 and appends [W0 Literal Shield WARNING] whenever any $W_0$ string literal is removed from a .py file, regardless of explicit contract overrides.

B.2 Scope-Qualified Summary of Observed Zero-Pass Clauses (development vs. validation)

Across 42 single-pass development runs (420 episodes), 9 / 50 clauses (21.50% weight; Clopper–Pearson 95% CI [0.00%, 8.41%]) had zero observed passes: 018 (case:citation_issue_set 3.40%, case:evidence_traceability 2.10%), 066 (case:first_seen_ledger 2.50%, case:component_state_reconciliation 1.50%), 080 (case:completion_and_unknown_outcome_safety 2.50%, case:evidence_and_storage_action_boundary 1.50%), 150 (case:trust_precedence_and_atomic_updates 2.50%, case:counter_backup_and_risk_policy 3.00%), and 154 (case:load_and_contract_safety 2.50%). Across 22 archived single-pass validation runs (880 episodes), 29 / 191 anonymized clauses (16.50% weight; Clopper–Pearson 95% CI [0.00%, 15.44%]) had zero observed passes. Because our strict firewall forbids inspecting hidden grader tests on either split or prompts/workspaces on validation, we do not attribute these 38 clauses solely to lexical non-closure: while actor-visible development contracts omit certain output tokens or field schemas (e.g., 066 classification values and 150 new rejection reasons), prior paired-checkpoint analysis (agent_harness_1 v3 [4], Section 4.6 & Table A3) established that compound checks on 018, 080, and 154 combine convention differences with substantive semantic and algorithmic discrepancies.

Reviewer report

Accept

This is a useful, bounded empirical and methodological contribution to understanding efficient harnesses. It does not demonstrate a new performance–cost frontier or a deployable router. Its contribution is to distinguish cross-package clause complementarity from sampling variation and task specialization, test a specification–grader mismatch under controlled conditions, and measure reasoning replay on a fixed lean harness. These findings have substantive relevance to deciding which harness interventions merit further investment.

The central mathematics is correct. Under the stated independent-draw model, the distinct-pair estimators are unbiased, the signed sample decomposition holds, and

$$ \Delta_{\mathrm{route}}^\star \leq \sqrt{D_{\mathrm{task}}} \leq \sqrt{\Delta_{\mathrm{div}}/2}. $$

The explicit negative-estimate example and the distinction between quadratic divergence and linear routing gains prevent important misinterpretations. My independent calculation from the retained clause vectors reproduced the pooled excess union of $0.78625$ percentage points, its nominal interval $[-1.02,2.59]$, the $7.7275$-point within-package gain, and the $27.81125\%$ joint failure rate. It also reproduced the cross-fitted routing gain of $2.8125$ points over the package average, with interval $[0.09,5.53]$. The latter is an informative diagnostic despite its uncertain advantage over Mode 50 alone.

The synthetic evidence is inspectable and supports the narrow conclusions. After inspecting the relevant code and retained programs, I re-graded all 160 final outputs and 120 reconstructed initial drafts with the supplied deterministic grader. Every final score matched; the only draft-to-final score change was the reported Mode 50 MO-1b improvement from $0.75$ to $1.00$. The seven initial MO-4 algorithm failures were distributed as reported: five in Mode 55 and one each in Modes 50 and 54. The specification and grader source establish that MO-4b deliberately removes three required reason literals while retaining exact-string grading. This is a controlled illustration of representation mismatch, not evidence that all persistent benchmark failures have that explanation.

Independent recomputation also reproduced Experiment W's $-0.20$-point score difference and $[-5.97,5.57]$ interval, and its solver costs agree with the retained token counts and price schedule. The decision not to advance replay under the declared gate is reasonable. The manuscript appropriately acknowledges that these data neither establish equivalence nor exclude its $+3.50$-point target. My checks reproduce calculations and deterministic grading of retained artifacts; they do not reproduce live model generation or independently authenticate the original execution history.

The distinction from previous work is sufficient, although the theoretical ingredients are classical. The published same-problem paper [4], especially Sections 4.6 and 4.10, already established convention-sensitive failures, within-package pair unions, and limited merging headroom. Papers [5], [7], and [8] supply the lean substrate, cost accounting, and related intervention evidence. The present cross-package bias-corrected analysis, same-task cross-fitting, controlled string-removal experiment, and replay intervention add evidence beyond those results. External literature likewise limits the novelty claim: unbiased quadratic two-sample statistics are established [11, 21], and learned cost-aware routing is established [22]. Here the novelty lies in the empirical application and distinctions between estimands, rather than a new statistical theory or routing algorithm. The cited self-correction literature [13–15] provides context without duplicating this particular intervention study.

The research questions, estimands, experimental comparisons, and decisive evidence are understandable in the main text. The paper is unusually dense and repeats many numerical results in the introduction and discussion, but this does not materially obscure the argument. The following clarifications would improve the accepted work:

  • Keep routing and union claims diagnostic. Cross-fitting holds out repetitions of the same task identities, not unseen tasks. The text acknowledges this; make it equally explicit wherever routing results are summarized. Clausewise union also assumes oracle access to which clauses pass and is not an implemented ensemble's score. No new prospective routing or composition benefit has been demonstrated.
  • Qualify confidence statements. The task-level Student-$t$ intervals and transformed routing upper limit are nominal approximations under the stated independence and stability assumptions. Concurrent scheduling alone does not establish whole-run exchangeability. For the pooled zero-pass results, explain the estimand across heterogeneous harnesses: the reported Clopper–Pearson limits are not bounds on every individual package, and the post-selected collection of zero-pass clauses does not receive simultaneous 95% coverage.
  • Narrow one causal sentence. Section 6.1 says the audit proves that specification placement caused guard variation. Draft timing rules out receipt-induced initial guards, but does not isolate the cause of their creation. Describe ambiguous placement as a plausible explanation unless a wording intervention is tested. The observed failure of receipts to repair these five guards remains supported.
  • Align presentation with the contribution. Shorten the metadata abstract and introductory numerical inventory, and describe the estimator as a classical U-statistic application. Adding the connection to linear-kernel squared mean discrepancy [21] and distinguishing same-task retrospective routing from learned prospective routing [22] would sharpen attribution.

[21] A. Gretton et al. A Kernel Two-Sample Test. Journal of Machine Learning Research, 13:723–773, 2012. https://www.jmlr.org/papers/v13/gretton12a.html

[22] I. Ong et al. RouteLLM: Learning to Route LLMs with Preference Data. arXiv:2406.18665, 2024. https://arxiv.org/abs/2406.18665

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