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Under review as a conference paper at ICLR 2027

Auditing Gradient Retention under Hidden Conditions: Exact Cancellation, Objective-Dependent Alignment, and the Limits of Kappa

Abstract

Learning systems often average gradients over hidden conditions: annotator groups with conflicting preferences, clients with different objectives, hidden teammates. When does averaging aggregate useful signal, and when does it suppress it? We show that gradient cancellation is governed by more than the presence of hidden heterogeneity. In an analytically tractable mirror model, elementwise parameter-independent weight fields cancel exactly under a symmetric condition mixture, while a differentiable-baseline field can retain a nonzero component away from uniform policies. For K-way mixtures retention depends on the mixture direction in the probability simplex at fixed distance from uniform, and objective-induced channels can interfere, making retention non-monotone in the entropy weight. A measurement protocol separates these structural effects from finite-sample noise: deterministic rollouts collapse retention into a weight ratio, and episode-noise readouts can understate it by an order of magnitude. Under a single bounded definition the retention score alone is ambiguous: a high score can be produced by condition-blindness rather than survival. In Overcooked the dynamic value field scores 0.998 while its condition contrast is only 0.1% of its shared mass; the differentiable-baseline advantage field carries a resolvable contrast (35–176x the estimation-noise floor, score 0.590) and the plain policy gradient's contrast sits at the noise floor (score 0.529). In 510K no field has a substantial condition contrast. The 30–65x value-policy gap suggested by noisy readouts is retired. A controlled capacity experiment shows that severe cancellation can coexist with poor worst-condition performance; in contrast, on a real three-group preference dataset the condition-contrast energy is dominated by item-level noise and group-conditioned capacity yields no gain. In a switching task, retention need not predict return when the measured condition is not the variable the task relies on. Retention is a structural audit of the specified condition signal, not a general performance metric, and it indicates when condition-aware capacity is likely worth its cost.

Primary area:
reinforcement learning
Keywords:
gradient conflict, hidden heterogeneity, gradient cancellation, policy gradient, value-based reinforcement learning, measurement and identifiability, group averaging

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_pURjOpenReview ↗
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1
Confidence
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1
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Paper summary

The paper studies gradient interference under different losses in reinforcement learning.

Critical strengths

None

Critical weaknesses

The manuscript as presented does not satisfy basic scientific standards of communication.

  • It is incredibly dense writing.
  • The text does not clearly establish what it attempts to do or why.
  • The text uses various terms without defining them. This starts in the title. I don't know what "the limits of kappa" means. This lack of definition includes terms such as retention which seems to be the main object of study.
  • Mathematical notation is not properly introduced.
  • Uncontextualized numbers are scattered everywhere (starting in the abstract). These may be referring to experiments that are not described or referenced.
  • The text references tools/settings that are never described such as a "mirror bandit".
  • The text states something about withdrawing claims but those claims never appear in the text (something about abelian groups).
  • The experiments are missing proper descriptions as to what the experiments are trying to do and how. The experiments seem largely to provide a collection of measurements of gradient norms.
  • As far as I understand, the math seems to be elementary vector cancellations, obfuscated simply by complex writing.

My review is not particularly detailed as the text is not readable. I believe extensive revisions are needed in terms of writing before it can be properly reviewed

Questions for authors

None

2 comments
AuthorsOpenReview ↗

Response to Reviewer pURj: a reading guide and concrete revision plan

We thank Reviewer pURj for the frank assessment. We agree that the paper is too dense, that several terms are used before they are defined, and that the abstract contains numbers without enough context. We will not argue with that; the revision will fix it. To make the current submission reviewable now, here is a short guide.

What the paper is trying to do, in five sentences.

  1. Training on a mixture of hidden conditions averages their gradients.
  2. We define retention kappa_mix = ||sum_i p_i g_i||^2 / sum_i p_i ||g_i||^2 (Eq. 1), bounded in [0,1].
  3. In a two-action mirror bandit, any parameter-independent elementwise weight field cancels exactly under a symmetric mixture; soft-Q has a closed form; K-way mixtures show direction dependence.
  4. Measurement matters: deterministic rollouts collapse kappa to a weight ratio; episode noise can understate it; fields must be compared on the same batch.
  5. Empirically, a high kappa can be condition-blindness rather than survival; DICES is a negative capacity check; retention is not a performance score.

Definitions that were missing or too late.

  • mirror bandit: two actions. Condition A has Q_A=(r,-r); condition B has Q_B=(-r,r); the condition is hidden; the mixture is symmetric.
  • retention / kappa: Eq. 1. It is a ratio of gradient energies, not accuracy, return, or a cosine similarity.
  • "limits of kappa": kappa alone cannot distinguish "condition signal survived" from "the field is condition-blind"; it must be read with E_contrast, contrast/noise, and contrast share.
  • "abelian groups": this sentence refers to an earlier version of the work, which claimed that direction dependence was specific to S3/non-abelian symmetry. That claim is withdrawn: the effect appears at K>=3 because of simplex geometry. In the revision we will remove the meta-reference and state the current claim directly.

Section map for the current PDF. §2 definitions and measured fields; §3 theory (Props. 1-4); §4.1 exact bandit; §4.2 protocol audit; §4.3 Overcooked/510K; §4.4 capacity; §4.5 DICES; §4.6 switching; §6 what the audit does and does not claim; §7 limitations.

On the math. The mirror-bandit algebra is intentionally elementary. The contribution is not a difficult theorem; it is the measurement argument: what a retention score can and cannot identify, and which protocol controls are needed to measure it. The complexity is in the interpretation, not the algebra. We will say this explicitly in the introduction.

Concrete revision plan.

  • Add a notation/glossary table at the start of §2 and define every symbol at first use.
  • Move the number-heavy sentences out of the abstract into a short "key findings" paragraph.
  • Add a one-paragraph reader's map at the end of the introduction.
  • Remove meta-references to withdrawn claims and state the current claims positively.
  • Add a "what this paper does not claim" box.
  • Cut redundant prose by about 15%.

We will upload the revised PDF before the end of the public discussion period. We are not asking for a score change. We would be grateful for a pointer to the first section where the reader loses the thread; that will help us target the rewrite.

AuthorsOpenReview ↗

Response to Reviewer pURj: a reading guide and a simplified revision

A short update to my earlier comment: that comment was written before the revision and described the plan; the revised PDF is now uploaded.

The revised paper:

  • replaces the vague "Limits of Kappa" in the title with "When Capacity Pays";
  • simplifies the abstract and adds a reader's map and a notation paragraph;
  • states the decision rule in one place: c/n_mean > 2, effect above the calibrated gate, and a task-relevant condition; retention is a diagnostic, not a gate;
  • adds §4.5 validation-selected capacity, §4.6 DICES, and §4.7 switching. The earlier references to "limits of kappa" and "abelian groups" are no longer in the paper; direction dependence is stated as K-way simplex geometry.

We have not added a full glossary in this revision; it is planned for the next version. The earlier comment remains for transparency; this note supersedes its section map and revision plan. No score request.

Reviewer_it9yOpenReview ↗
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2
Confidence
2
Informativeness
2
Presentation
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Soundness
2
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Paper summary

This paper studies gradient cancellation when training data mixes hidden conditions. It gives exact results for mirror and K-way bandits, and measures retention together with condition contrast and noise in RL tasks and DICES-350

Critical strengths
  1. The exact bandit results make the role of the objective clear. The stochastic rollout controls also show how the measurement protocol can change the reported score.

  2. The paper shows that high retention can come from condition-blind gradients. Comparing fields on the same episodes and reporting contrast and noise helps avoid misleading comparisons.

Critical weaknesses
  1. Inconsistent noise comparison: Table 5 compares condition contrast with per-item variance, while the proposed rule uses the noise of estimated condition means. A contrast smaller than item variance may still be measured reliably. The conclusion that DICES needs no conditional capacity is therefore not well supported.

  2. Limited support for the capacity rule: The positive result is on an exact matching bandit where the condition determines the correct action. The real tasks do not show that the audit can predict a useful capacity change.

  3. Missing noise estimates: The paper does not give the formula for contrast-to-noise or the episode counts for Tables 2–3. Several conclusions depend on ratios near 1, but uncertainty in these ratios is not reported.

  4. Source of the awr contrast: Table 2 differentiates through the value baseline, and Section 7 notes that the fields use different parameter supports. Without a breakdown by parameter group, it is unclear how much of the awr contrast comes from the policy versus the value head.

Questions for authors
  1. How are the noise floor and contrast-to-noise computed? Does the DICES conclusion hold when using the noise of condition means?

  2. Does the Overcooked awr contrast remain when excluding value-head parameters or detaching the baseline?

  3. Further validation: Is there a real task where the audit predicts a gain from conditional capacity?

1 comment
AuthorsOpenReview ↗

Response to Reviewer it9y: DICES noise, AWR support, and a real-task positive

We thank Reviewer it9y. Points 1 and 4 identified real inconsistencies; we ran the exact checks, corrected the paper, and added a real-task validation.

W1/Q1: noise comparison. The rule uses the noise of estimated condition means, c/n_mean=E_contrast/(sum_i p_i^2 sigma_i^2/n_i), while the DICES table compared E_contrast with sigma^2 (item variance). With n=245 training items per group, DICES c/n_mean is 122±5 (race), 28±5 (age), 75±5 (gender): the contrast is statistically resolvable. E_contrast/sigma^2 is 0.168/0.037/0.153, an effect-size ratio, not a significance test. We report both and use a two-gate rule: c/n_mean>2 and effect above a calibrated gate (about 0.3-0.4). DICES passes the first and fails the second. The original one-gate rule would have recommended intervention on DICES; that false positive motivates the second gate. The negative capacity result survives empirically (group-conditioned, group-threshold, reweighting, and DRO all fail), but the reason is effect size, not unresolvability. We do not defend the original wording.

W4/Q2: AWR decomposition. You are right that the full-vector AWR contrast comes from the value head. We decomposed the gradient by parameter support on the same batches (3 seeds, 40 episodes/condition): dynamic full kappa 0.581/0.571/0.619; policy-support 0.638/0.572/0.474 with c/n 0.88/1.45/1.76; value-support c/n 191/125/36. Static full/policy/value kappa 0.500; policy c/n 0.87/0.90/0.57; value c/n 57/48/7. Detaching the baseline leaves the policy-support field unchanged because PPO's value head is a separate critic, not V^pi=sum_a pi(a)Q(a). To instantiate the analytic exception we train a post-hoc Q(s,a) head with expected SARSA and use V=sum_a pi(a)Q(a); the actor-support c/n becomes 4.19/5.48/2.79 (mean 4.15), while the detached baseline is 0.68/0.95/1.17 (mean 0.93). The original 35-176x number is a value-head contrast; the policy-dependent baseline gives a smaller but resolvable 2.8-5.5x actor-support contrast. We relabel the entry, remove the "only non-value field" claim, and keep the analytic exception as a bandit result that the Overcooked value-head experiment does not instantiate.

W3: formulas and counts. c/n_mean=E_contrast/(sum_i p_i^2 sigma_i^2/n_i). Overcooked: n=40 episodes per condition per checkpoint, 3 seeds; 510K: n=60 per checkpoint, 6 seeds per visibility level; DICES: n=245 training items per group, 3 seeds. The new fixed-partner capacity result uses 40 validation and 100 disjoint test episodes per condition, 3 seeds. We will add the counts to the captions and report bootstrap CIs.

W2/Q3: real-task capacity. The revision now has a real-task positive: fixed-partner Overcooked, shared vs conditional vs specialist, validation- selected routing. It improves average return by 33.5 and worst-partner return by 41.9 across three seeds (100 test episodes per condition). Naive conditional and specialist training collapses in two of three seeds; the router rejects failed models on validation and falls back to shared. This is not a claim that naive conditional capacity is stable; it is a claim that the audit identifies when capacity is worth trying, and validation is needed to confirm it. The controlled positive control on DICES text features calibrates the effect-size gate; DICES itself remains the negative boundary.

We appreciate the reviewer's help; the corrections make the claims narrower but more defensible, and the new positive result answers the real-task question.

Reviewer_AZi7OpenReview ↗
Rating
2
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies how averaging gradients over hidden conditions can preserve or cancel condition-specific signal. It derives exact results for mirror and matching bandits, analyzes objective-dependent retention and mixture geometry, and corrects rollout and noise-related measurement artifacts. Its central argument is that retention must be interpreted alongside condition contrast and estimation noise: high retention can reflect condition-blindness rather than preserved signal. Overcooked, 510K, a controlled capacity experiment, DICES-350, and a switching task illustrate the diagnostic’s usefulness and limitations. The paper presents retention as a structural audit, not a general performance metric.

Critical strengths
  • S1. The distinction between retention, condition contrast, and estimation noise is consequential. In dynamic Overcooked, the diagnostic value field has retention of 0.998 but contrast of only about 0.1% of its shared energy. This concretely demonstrates why high retention alone does not establish preservation of useful condition signal.

  • S2. The measurement audit provides practical value. It shows how deterministic rollouts distort retention and episode noise depresses measured scores. The paired field comparisons and correction of the companion report’s 30–65× value–policy gap clarify which findings survive a consistent measurement protocol.

Critical weaknesses
  • W1. The operational decision rule is not sufficiently calibrated. The finite-sample analysis provides a surrogate rather than a high-probability guarantee, while the real-environment evidence uses limited seeds and one supervised dataset. Overcooked compares contrast against mean-estimation noise, whereas DICES compares it against within-group item variance. Without connecting these quantities and their sample-size dependence, it remains unclear how reliably the audit supports intervention decisions.

  • W2. The intervention recommendation is stronger than the comparative evidence. Conditional capacity succeeds in the controlled matching task, but this does not establish it as the indicated remedy across settings. DICES uses a linear model without reweighting or group-DRO comparisons. The paper therefore establishes a useful diagnostic more convincingly than a capacity-specific prescription. Comparisons with alternative interventions would materially strengthen the practical conclusion.

Questions for authors
  • Q1. How should the mean-estimation noise criterion in Overcooked be reconciled with the item-variance comparison in DICES? Please clarify sample-size dependence and provide finite-sample calibration or explicitly limit the criterion to a screening heuristic.

  • Q2. What outcome would falsify the operational rule? If low retention, resolvable contrast, and task relevance coexist but conditional capacity provides no benefit, how would you distinguish failure of the audit from failure of the intervention?

  • Q3. Are the dynamic Overcooked conclusions stable across additional seeds, checkpoints, and evaluation batches? Please report whether the value field’s negligible contrast and the differentiable-baseline advantage field’s resolvable contrast persist.

  • Q4. Can reweighting or group-DRO address the same diagnosed failure without additional conditional capacity? Without comparative evidence, would you narrow the recommendation to an intervention demonstrated in the controlled matching task rather than the generally indicated remedy?

  • Q5. The paper explicitly limits the value-field result to the diagnostic gradient of −∑tV(st)-\sum_t V(s_t). Does the finding extend to TD-residual or actor-critic value gradients, or should its practical interpretation remain specific to that diagnostic field?

4 comments
AuthorsOpenReview ↗

Response to Reviewer AZI7: calibrated rule, falsification, and a real-task positive

We thank Reviewer AZI7. We agree the decision rule, not the diagnostic, was the weak point. The revision adds the missing calibration, comparative interventions, and a real-task validation.

W1/Q1: two noise scales. The paper uses c/n_mean = E_contrast/(sum_i p_i^2 sigma_i^2/n_i) for the noise of estimated condition means, and sigma^2 for within-condition item variance. These answer different questions. In Overcooked n=40 per condition, c/n_mean is the relevant floor. In DICES n=245 per group, c/n_mean is 122±5 (race), 28±5 (age), 75±5 (gender): the contrast is statistically resolvable. The original table compared E_contrast with sigma^2 (0.17/0.04/0.15), which is an effect-size ratio, not the mean-estimation floor. We now report both and use a two-gate screen: c/n_mean>2 and effect above a calibrated threshold. The controlled positive control places the practical gate near 0.3-0.4: no gain at effect 0.18, gain at 0.42. DICES race is 0.168, below the gate. The original one-gate rule would have recommended intervention on DICES; that false positive is why the second gate is needed. We are correcting the rule, not claiming post-hoc success.

W2/Q4: comparative interventions. On DICES race, group-conditioned models, group-specific threshold calibration, group-balanced reweighting, and a group-DRO surrogate all fail to improve held-out average/worst-group accuracy (shared 0.655/0.609; conditional 0.653/0.607; threshold 0.656/0.605; reweighting 0.652/0.606; DRO 0.655/0.609). The negative side is therefore not an optimizer issue. On the positive side, fixed-partner Overcooked now gives a real-task result: validation-selected conditional routing improves average return by 33.5 and worst-partner return by 41.9 across three seeds (100 test episodes per condition). Naive conditional/specialist training collapses in two of three seeds; validation rejects the failed models and falls back to shared. The recommendation is therefore a two-gate screen plus a validation guard, not unconditional capacity.

Q2: falsification. The rule is falsified by a setting where (a) c/n_mean>2, (b) effect is above the calibrated gate, and (c) the condition is task-relevant, yet a capacity-matched conditional model does not improve worst-condition performance while a capacity control shows it can fit the condition-specific signal on training data. If the conditional model cannot fit even on training data, the intervention failed, not the audit. DICES fails (b), so it is an effect-size boundary, not a falsifier of the resolvability gate. The fixed-partner positive is the complementary high-retention case: kappa 0.946, but a 5.4% contrast share and effect 1.60; retention is therefore a diagnostic, not a gate.

Q3: stability. The switch-kappa protocol uses 8 seeds (static 0.533±0.068, dynamic 0.502±0.196); dynamic plain-gradient c/n is 0.17-2.02, at the noise floor; static is 3.1-461. The field axis uses 3 seeds. The new fixed-partner capacity result uses 3 seeds and 100 test episodes per condition. We will add bootstrap CIs and the remaining field-axis checkpoints. One correction from this check: the full-vector AWR contrast is value-head dominated; actor-support is at the floor, and a policy-dependent baseline gives 4.15x. We no longer use the full-vector AWR as a non-value field.

Q5: TD residual. The measured value field is -sum_t V(s_t), not a TD residual. A TD residual with a detached critic is a critic field; with a shared/differentiable critic it can inherit policy dependence, but we have not measured it. We add a scope remark and do not claim extension to actor-critic TD gradients.

We appreciate the reviewer's help in making the audit's limits and its positive use explicit.

Thank you for the detailed response. I have read the revised manuscript and appreciate the correction to the DICES noise interpretation: the group differences are resolvable, although the conditional model still does not yield a clear benefit. I also appreciate the clarification that the previously reported 35–176× contrast in Overcooked mainly comes from the value head, rather than the policy component. These corrections have helped me better understand the results.

The added reweighting and group-DRO-style comparisons, together with the fixed-partner Overcooked experiment, also strengthen the discussion of intervention effects. The authors have clarified that TD-residual gradients were not measured and that conditional models require validation and a fallback. These additions and scope clarifications address my main concerns.

I have two brief questions:

1. The authors mention that they will add bootstrap confidence intervals and more checkpoints for Overcooked. Are these results available now, and are they consistent with the findings reported in Section 5.3 of the revision?

2. Section 6 presents a screening rule based on a calibrated threshold, which was mainly obtained from one controlled experiment. Do the authors expect this threshold to apply directly to other tasks? If this is not yet clear, I suggest noting when introducing the rule that it may need to be recalibrated for other tasks.

AuthorsOpenReview ↗

Follow-up to Reviewer AZI7: stability check and threshold calibration

We thank the reviewer for the follow-up.

Q1: additional checkpoints / bootstrap. The extra field-axis checkpoints are now available (seeds 42, 43, 45, 46, 47 added to 41, 44, 48; same shared-episode protocol). The 8-seed results are consistent with the 3-seed numbers in Section 5.3:

  • Dynamic value: kappa 0.998 (range 0.998-0.999); c/n mean 9.7 (range 1.5-33.6; checkpoint-level bootstrap 95% CI for the mean 4.1-17.3); contrast share 0.15% (0.11-0.17%); effect mean 0.12 (range 0.02-0.42).
  • Dynamic reinforce: c/n mean 1.2 (range 0.85-1.87; bootstrap CI 1.0-1.4), at the noise floor.
  • Static value: c/n mean 8750 (range 443-30473; bootstrap CI 3480-15716), the visible-condition measurement control.

The 3-seed numbers in Section 5.3 are unchanged; the 8-seed check supports the same qualitative reading. One dynamic-value seed reaches the effect gate (0.42); because the start partner is task-relevant for only the first 30 steps, this reinforces the condition-relevance caveat rather than a capacity recommendation. The bootstrap here is over checkpoints (8 seeds); we can add episode-level CIs if the reviewer prefers.

Q2: threshold calibration. We agree. Section 6 now states that the exact gate is a screening convention calibrated on one controlled sequence, should be recalibrated for a new task, and that the continuous c/n and effect ratios are the primary readout. The validation/fallback step is also task-specific.

We appreciate the reviewer's help in making the scope of the rule explicit.

Thank you for the additional results.

The eight-seed analysis is consistent with the findings in Section 5.3. The dynamic value field still shows near-unity retention with a small contrast share, and the REINFORCE contrast remains close to the noise floor. The bootstrap results also help confirm the stability of these observations.

Your clarification on the effect-size threshold addresses my second question. Treating it as a task-specific screening heuristic and explicitly noting the need for recalibration in Section 6 makes the scope of the rule clear.

These additions have addressed my follow-up questions. I appreciate the effort put into the revisions.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Reader's guide, corrections, and new positive results

We thank all reviewers. We have uploaded a revised PDF; the title keeps the original stem and replaces the vague "Limits of Kappa" with "When Capacity Pays." The core thesis is unchanged, but two measurement interpretations are corrected and two positive validations are added. This comment is a one-page guide.

What the paper asks (five sentences).

  1. Training on a mixture of hidden conditions averages their gradients.
  2. We define retention kappa_mix = ||sum_i p_i g_i||^2 / sum_i p_i ||g_i||^2 (Eq. 1), bounded in [0,1].
  3. In a two-action mirror bandit, parameter-independent elementwise weight fields cancel exactly under a symmetric mixture; soft-Q has a closed form; K-way mixtures show direction dependence and channel interference.
  4. Measurement matters: deterministic rollouts collapse kappa to a weight ratio; episode noise can understate it; fields must be compared on the same batch.
  5. A high kappa can be condition-blindness rather than survival. Read kappa with condition contrast, estimation noise, and effect size; this gives a two-gate decision rule for condition-aware capacity.

Definitions.

  • condition i: hidden group; p_i: mixture weight; g_i: condition-i gradient.
  • kappa_mix: shared energy / mixture energy; not accuracy, return, or cosine.
  • c/n_mean = E_contrast / (sum_i p_i^2 sigma_i^2 / n_i): resolvability of the estimated condition means.
  • effect = E_contrast / sigma^2: between-condition signal relative to within-condition item noise.
  • contrast share = E_contrast / E_mix; a small share with high kappa can mean condition-blindness or a non-task-relevant condition.
  • mirror bandit: two actions, Q_A=(r,-r), Q_B=(-r,r), hidden condition, symmetric mixture.
  • retention is a decision aid: kappa alone cannot distinguish survival from condition-blindness or mismatch; read it with contrast, c/n, and share.

Section map (revised). §2 definitions/fields; §3 theory (Props. 1-4); §4.1 exact bandit; §4.2 protocol audit; §4.3 Overcooked/510K; §4.4 capacity; §4.5 validation-selected capacity on a real task; §4.6 DICES; §4.7 switching; §6 claims; §7 limitations. Main text ends on p. 10.

What changed. (1) DICES noise. The paper compared E_contrast with sigma^2 and called it the noise floor. The correct mean-estimation floor gives c/n_mean=122/28/75; the contrast is statistically resolvable. Its effect size is 0.17/0.04/0.15, below the calibrated gate, so DICES is a boundary negative, not an unresolvable contrast. (2) AWR support. The full-vector AWR contrast is carried by the value head; actor-support c/n is 0.88/1.45/1.76. A policy-dependent V=sum_a pi(a)Q(a) baseline gives a smaller but resolvable actor-support contrast (2.8-5.5x, mean 4.15), while detaching the baseline leaves it at 0.93. The original 35-176x number is a value-head contrast, not a policy signal. (3) Controlled positive control. On real DICES TF-IDF features with a controlled group-dependent label, capacity gains appear when E_contrast/sigma^2 exceeds about 0.4; at 0.18 there is no gain. This calibrates the effect-size gate. (4) Real-task validation. On fixed-partner Overcooked, validation-selected conditional routing improves average return by 33.5 and worst-partner return by 41.9 across three seeds (100 disjoint test episodes per condition). Naive conditional and specialist training collapses in two of three seeds and is rejected by validation; the router falls back to shared. (5) We relabel dynamic Overcooked as a condition-relevance boundary: the start-partner condition covers only the first 30 steps, so its negligible contrast is not evidence that the value field is blind to a relevant hidden partner; the fixed-partner audit does detect one.

The decision rule is now: c/n_mean>2 + effect above the calibrated gate + task-relevant condition; retention is a diagnostic of the regime, not a gate. Then validate the conditional model and fall back to shared if it fails. We are not asking for a score change; we welcome pointers to the first unclear section.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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