acceptodds
Under review as a conference paper at ICLR 2027

When Can a World Model Decide? Certifying Elite Decisions in Sampling-Based Planning

Abstract

Sampling-based planners such as CEM and MPPI turn a latent world model into a controller by trusting its ranking of candidate action sequences at every iteration. We show when that trust is warranted. A rollout error bound yields a decision certificate: the model places a candidate correctly in or out of the elite set whenever the candidate lies more than twice the error from the elite boundary. Executing every candidate a planner evaluates on Push-T, we find that the certified fraction falls from 0.67 to 0.29 over the search: the planner converges until its candidates differ by less than the model can resolve, and more search cannot recover the lost resolution. The certificate also names the remedy, a more accurate predictor or models with independent errors, and only the decisions at the elite boundary need it. We introduce EliteCert, in which the planning model screens every candidate and independently trained validator models re-score only a calibrated band around the K-th elite. EliteCert enters through the cost function, so CEM, iCEM and MPPI run unmodified. Under the official LeWM protocol it raises success by 9–14 points for all three planners on Push-T and by 2–3 points on Cube, beats the default configuration at 44% of its CPU time, matches re-scoring every candidate at a third of the extra compute, and adds a further 1.8 points to a planner whose predictor we retrained. An offline qualification test tells in advance which models can serve as validators. Finally, we prove and measure that gains on logged candidate pools do not transfer to the closed loop of an iterated planner, and evaluate every claim in the closed loop, with 1800 paired runs behind each headline comparison.

Primary area:
reinforcement learning
Keywords:
world models, model-based planning, cross-entropy method, MPPI, ensembles, JEPA

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_HGJEOpenReview ↗
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3
Confidence
3
Informativeness
2
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2
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Paper summary

This paper investigates how prediction errors in world models influence the selection of candidate action sequences by sampling-based planners. Through error analysis, the authors derive sufficient conditions for "elite-set" decision-making, which ensuring that the optimal action sequence remains within the chosen subset, and propose EliteCert. This approach uses a primary model to filter candidates, followed by a secondary, independent verification model to re-score those candidates that could potentially alter the composition of the elite set. Experimental results demonstrate that this method improves closed-loop control performance while requiring less additional computation compared to evaluating the entire candidate set.

Critical strengths
  • The research question is valuable. By linking world model errors to the candidate selection process of a planner, the study offers a clear perspective on why the returns from increasing the search budget eventually saturate.

  • The methodology is sound, and the experiments are robust. The selective re-ranking design is intuitive; the experimental evaluation includes closed-loop validation, comparisons of computational overhead, and rigorous baselines using single-model approaches. Furthermore, the authors document instances where the verifier fails or offline performance gains fail to generalize, which strengthens the credibility of their conclusions.

Critical weaknesses
  • The attribution of certain performance gains remains insufficiently explained. For MPPI methods that rely on the magnitude of cost values, normalization can alter the weights assigned to candidate trajectories; therefore, it is necessary to further disentangle the effects of ranking adjustments from those resulting from changes in cost scaling.

  • The scope of applicability remains limited. Evaluations have focused on simulation tasks within a single world-model framework, and the observed gains depend on the availability of a suitable verifier. Furthermore, the reliability of candidate filtering and bandwidth calibration under distribution shifts remains unclear.

Questions for authors
  1. For MPPI, is it possible to disentangle the performance gains, attributable to re-ranking versus those resulting from changes in weight scaling, by using a control baseline normalized by the same cost criteria?

  2. When should the validator qualification test and calibration bandwidth be re-evaluated following shifts in task distribution or changes to the model? What are the applicable boundaries for these methods, based on existing results?

2 comments

Thank you for the insightful review. Please also see Point 1 of our General Comment, which contextualizes the headline Push-T numbers against stronger single-model baselines.

W1 / Q1. Separating elite re-ranking from cost scaling in MPPI. We ran the exact closed-loop control experiment you suggested (Section 6.1, Appendix E.2). In MPPI, returned costs c~i=sd⁡B(c) si\tilde c_i = \operatorname{sd}_B(c)\,s_i affect both which KK candidates are selected and the softmax weight spread (sd⁡B(s)<1\operatorname{sd}_B(s) < 1 when models disagree). We evaluated two controlled arms on the identical 600 Push-T tasks, 3 planner seeds (1,800 paired runs/arm), temperature, band, and model calls:

MPPI arm (Push-T, 150x10, 1,800 paired runs)Success (%)vs. Official alone
Official planning model alone (native)63.9—
Spread only (planner's elite ordering, ensemble's cost spread)63.7-0.2 [-1.8, +1.5]
Ordering only (ensemble's elite ordering, planner's cost spread)76.2+12.3 [+9.6, +14.9]
Deployed EliteCert (both ordering and spread)77.7+13.8 [+11.2, +16.3]
  • Result: Elite re-ranking alone recovers 89% of the gain (+12.3 of +13.8 pp), whereas compressing the cost spread alone contributes nothing (-0.2 pp; deployed beats ordering-only by a further +1.5 [+0.1, +2.9] pp). Thus, MPPI's improvement is decisively attributed to candidate re-ranking.
  • Single-model context: Evaluating the public validators alone with native MPPI reaches up to 69.7%, so EliteCert still adds a substantial +7.9 [+5.5, +10.4] pp over the best single model on MPPI (Table 2).

W2. Empirical scope. We agree that our evaluation is scoped to LeWM latent world models, simulated benchmarks, and settings where an error-diverse validator exists (stated explicitly in Section 8). Within this scope, two new results clarify the picture: (i) against the strongest single model, ensemble gains are +2.3 pp for CEM (150x10), +7.9 pp for MPPI, and -0.4 pp for iCEM; and (ii) at the default 300x30 budget—where native search has saturated—EliteCert reaches 95.4%, adding +2.2 [+0.9, +3.6] pp over the best single checkpoint at 300x30 (Table 2).

Q2. When must qualification and band width δ\delta be re-evaluated, and what are the boundaries? Section 6.3 and Appendix E.1 now establish concrete empirical boundaries. Both checks should be re-evaluated when the planning model, validator set, task distribution, or search budget (N,K,T)(N,K,T) changes:

  • Deployment shift (native →\to EliteCert pools): Conservative—fixed δ=0.481\delta=0.481 (90% offline target) covers 91% [89, 92] of promotions under native CEM and 93% under EliteCert across the 600 official tasks.
  • Stronger planning model: Also conservative (96%–97% coverage with retrained predictors as planners, as promotions become fewer and closer to the cut-off).
  • Larger search budget (N,K,T)(N,K,T): Under-covers. Scaling from 150x10 to 300x30 drops coverage of δ=0.481\delta=0.481 to 84% overall and 73% at iteration 29; offline recalibration yields δ=0.657\delta=0.657 (restoring 90% coverage), used in our 300x30 closed-loop run.
  • Cheap online recalibration: Monitoring requires model evaluations only (no simulator resets). Passively scoring full pools on 20 tasks calibrates δ=0.45±0.10\delta = 0.45 \pm 0.10, achieving 89±4%89 \pm 4\% promotion coverage on the remaining 580 tasks. Moreover, closed-loop success does not differ between calibrated 80% and 90% widths (δ=0.296\delta=0.296 vs. 0.4810.481: -0.3 [-1.3, +0.8] pp), so δ\delta primarily governs validator compute.
  • Qualification boundaries: Admission decisions are invariant across i.i.d., block-correlated, and temporally smoothed action perturbations (scales 0.05–0.2), though untested under task-distribution shift. Window-bootstrap 95% CIs on Δq\Delta q have half-width ±0.01–0.02\pm 0.01\text{--}0.02, so margins within ±0.02\pm 0.02 of zero are statistically ambiguous and treated cautiously (Section 6.2).

Thank you to the authors for the late response. Your response have addressed most of my concerns.

The description in response 2 doesn't seem to directly prove that a sufficiently high band width coverage is linked to a validator being qualified, does it?

I choose to keep my intial score.

Reviewer_qJYSOpenReview ↗
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Paper summary

The paper addresses the issue of action-candidate generation by sample-based planners. The goal of these planners are to generate actions to be used for search in a given problem in order to identify the best action to be taken in the problem. The planners iteratively generate actions from a distribution and use KK of these actions to update the sampling distribution. The problem is when these KK actions are too similar, resulting in a degenerate sampling policy. As I understand it, this paper introduces a technique to increase the coverage of the KK actions by looking at the errors of the action trajectories. The paper tries provides empirical result to demonstrate the effectiveness of the proposed idea.

Critical strengths

The idea of using error-bounds on the predictive trajectories to differentiate between actions to sample is an interesting one.

Critical weaknesses

The paper is nigh incomprehensible. I cannot even say with surety whether I actually understood what it claims to show.

  • Most of the terminology and notation used is not what is conventional in the field nor defined for the paper.
  • The terminology used is also inconsistent or changes throughout the paper. In technical writing, it is always advised to use a single term to describe something and then repeatedly use that one term. Or at least provide exact definitions of the terms being used. For example, I could not keep track of "band", "pool", "gate" because they seemed to be used interchangeably at times and differently at times.
  • The terminology also sometimes seem counterintuitive --- the "elite" set reads as if the KK actions are the best actions and not that these actions are the most disparate from each other (at least, I think ultimately that is what the paper is trying to say.)
  • There are a number of statements that are too long to follow and some that do not make sense. For example, I don't understand what this statement in line 232 means: "the small shortfall against nominal reflects gaps the cluster within pools."

Because of these and other similar issues, I am not quite sure what the paper is purportedly trying to do. As I get it, the method boils down to:

  1. we need diverse actions for sampling,
  2. we can increase diversity by selecting actions that have higher error differences from one another,
  3. we use multiple models to estimate the values of actions in improve accuracy.

The way the paper is written, only an expert in working specifically with these algorithms or these domains would understand.

The main theoretical statement of the paper is Theorem 1 seems like a trivial statement that actions with similar values will be closer together within certain bounds. Unless I am missing something, this does not seem like a significant theoretical contribution. I am not a math person, but it also seems like the theorem is incorrect --- the statement looks like it only holds true if predictive errors rise from overestimation of the action values.

I cannot assess whether the experimental results support the paper's claims.

  • The evaluation domains are not described so I cannot assess whether they are appropriate for the proposed methods.
  • The baselines are not described (in fact, the paper only ever uses the acronyms for the other methods and never fully names them).
  • The evaluation metrics are not described so the reader would not know what the numbers mean.

Additionally, a large swathe of results are referred to in the appendix. The appendix is not a loophole for adding more pages to a paper; it is supposed to contain information that supplement the main body/results of the paper. The paper should contain the main results in the main portion of the paper.

The mathematical portion is also poorly written. There occurences of notation not being explicitly defined, e.g., fθf_\theta, pθp_\theta, BδB_\delta. zz is over-loaded for embeddings and costs.

Questions for authors

I have no questions that affect my assessment.

1 comment

Thank you for your candid review. Your summary made it clear that our original writing failed to communicate even the basic problem setup, leading to a reasonable misreading of the method. We have completely rewritten the main text from scratch to fix this, and we would be very grateful if you could glance at the first three pages of the revised PDF.

1. What the paper is actually about (in plain terms). At each step, a sampling-based planner (such as CEM) samples NN candidate action sequences, predicts the cost of each using a learned world model, keeps the KK sequences with the lowest predicted cost (standardly called "elites" in CEM—diversity plays no role), and refits its Gaussian sampling distribution to those KK sequences. As iterations progress, candidates cluster together until their true outcome differences are smaller than the world model's prediction error, causing the model's ranking near the top-KK cut-off to break down (which we measure directly by executing all candidates in the simulator). EliteCert is a simple wrapper: the planning model still scores all NN candidates, while independently trained world models (validators) re-score only candidates near the top-KK cut-off, keeping the KK lowest-average-score sequences. Figure 1 illustrates a single iteration step by step.

2. Unified terminology and notation (Table 1). Every concept now has a single name defined once in Table 1: candidate pool (NN sequences in one iteration), elite set (KK lowest-cost sequences), elite cut-off (KK-th lowest cost), re-scoring band (candidates within δ\delta standard deviations above the cut-off), validator, promotion, and qualification test. The overloaded term "gate" has been removed from the main text; latent embeddings (zz), model costs (CC), and standardized ensemble scores (ss) use distinct symbols; and opaque sentences such as line 232 were completely rewritten.

3. Does Proposition 1 assume overestimation? No—errors of either sign are allowed. Proposition 1 assumes ∣Cθ(a)−J(a)∣≤ε\lvert C_\theta(a) - J(a) \rvert \le \varepsilon for predicted cost CθC_\theta and true cost JJ. If J(ai)<J(aj)−2εJ(a_i) < J(a_j) - 2\varepsilon, then Cθ(ai)≤J(ai)+ε<J(aj)−ε≤Cθ(aj),C_\theta(a_i) \le J(a_i) + \varepsilon < J(a_j) - \varepsilon \le C_\theta(a_j), where the factor of 2ε2\varepsilon simultaneously covers overestimating aia_i by ε\varepsilon and underestimating aja_j by ε\varepsilon. This 3-line proof now appears inline in Section 3. We completely agree that the inequality is elementary: we downgraded it from "Theorem" to Proposition 1, use it strictly as a yardstick (2ε2\varepsilon) for the simulator audit in Section 4, and renamed marked candidates "empirically resolved" rather than "certified."

4. Self-contained tasks, baselines, planner names, and main-text results.

  • Planners: Cross-entropy method (CEM), improved CEM (iCEM), and model predictive path integral control (MPPI) are defined in full in Section 2.
  • Tasks, metric, and baselines: Section 6 defines Push-T, Cube, and Reacher, the success metric (% of episodes passing the environment's goal check within 50 steps), and all baselines (native planners across search budgets, individual validators/retrained predictors alone as planners, fixed top-2K2K re-scoring, full-pool re-scoring, and MC-dropout copies).
  • Main results in the main text: All primary closed-loop comparisons now sit in Tables 2, 3, and 4 in Section 6, with seed breakdowns and ablations in the Appendix.

5. Calibrated empirical claims. As detailed in Point 1 of our General Comment, adding single-validator planner baselines shows that over the strongest single model, EliteCert adds +2.3 pp with CEM at 150x10 (+2.2 pp at 300x30, reaching 95.4%), +7.9 pp with MPPI, and -0.4 pp with iCEM. We hope the revised manuscript now presents both the diagnostic findings and these controlled results clearly and transparently.

Reviewer_eyNZOpenReview ↗
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Paper summary

The paper asks when the ranking a latent world model feeds a sampling-based planner (CEM, iCEM, MPPI) can be trusted. Theorem 1 turns a standard rollout-error bound into a decision certificate: a candidate lands on the right side of the elite boundary as long as its true value is more than twice the model's error away from it. To see how often that holds, they executed every candidate a real CEM run evaluated, 561 decisions on Push-T, and the certified fraction falls from 0.67 in the first iteration to 0.29 in the last, with plan quality flat after half the default budget. Late in search, what binds is the model's resolution, not the budget. Their fix, EliteCert, touches only the cost function. The planner scores everything as usual, but a few independently trained validators re-score a narrow band around the elite cut-off; how wide that band is comes from a coverage target on measured promotion gaps, and an offline test decides which models qualify. If none qualify, the planner runs bit-for-bit as before. Under the official LeWM protocol this adds 8.7, 12.4, and 13.8 points to CEM, iCEM, and MPPI on Push-T and 2-3 on Cube, and it beats the default 300-candidate, 30-iteration configuration while using 44% of its CPU time.

Critical strengths
  1. The closed-loop methodology. Every headline comparison is 1800 paired runs, and the paper is built so that offline wins cannot sneak past as real ones (Prop 1, plus five measured failures, plus a held-out set never used for any choice). I do not often see this level of care, and it is the main reason I believe the +9-14 point numbers.
Critical weaknesses
  1. The method needs several competent world models that were trained independently. Where those do not exist (Reacher), the gate abstains and there is no gain. The retrained-predictor route is the practical fallback, but on Reacher it gives +1.2 at one seed (p=0.66) and +2.2 over three (p=0.059), which is thin. If you have one in-house model on a new domain, the paper does not yet show a path to the headline gains.
  2. The formal results are light. Theorem 1 is a standard compounding bound, Proposition 2 is elementary, and the ε used at deployment is an empirical median residual, not a bound (4-12% of certified decisions wrong). The paper says so plainly, and I appreciate that. Still, readers looking for an actual guarantee should know the weight sits on the experiments.
Questions for authors
  1. The Push-T validators are decent planners themselves (77-79%). How does the gain behave as validator quality drops toward the qualification threshold? For retrained predictors, which pass at equality on Reacher, is there a relation between the offline q₀.₁ margin and the closed-loop gain? That would tell practitioners when retraining is worth the trouble.
  2. δ is calibrated on native planner pools, and coverage goes up on certified-run pools, so the miscalibration is conservative. What about a bigger shift, say swapping in a much stronger planning model? Does the band under-cover, and is there a cheap online check?
  3. Could ε and the band be estimated online by replaying a small candidate subset, removing the offline audit? Even a rough measurement would tell me whether this can maintain itself in deployment.
1 comment

Thank you for your detailed review; your questions shaped most of our new experiments. Please see Point 1 of our General Comment first, which directly addresses W1.

W1. Reliance on competent, independently trained models; single-model baselines. We agree completely, and new baselines make this concrete:

  • Public validators alone: As you noted, the Push-T validators are strong planners themselves—reaching 87.4%–88.9% alone with CEM (vs. 82.5% official), while one predictor retrained on the official frozen encoder reaches 89.3% at zero extra planning cost. Upgrading the single model is thus always the first step.
  • Ensemble gain over best single model: Over the strongest single checkpoint, EliteCert adds +2.3 [+0.7, +3.8] pp with CEM at 150x10 (+2.2 pp at 300x30, reaching 95.4%), +7.9 [+5.5, +10.4] pp with MPPI, and -0.4 [-2.8, +1.9] pp with iCEM.
  • In-house retraining only: Among our three retrained Push-T predictors, a qualified setup (weakest predictor by q0.1q_{0.1} plans; the other two validate) reaches 90.5%—adding +1.8 [+0.6, +3.1] pp over its own planner and +1.2 [-0.2, +2.6] pp over the best single predictor (Table 3). On Cube, shared-encoder predictors share the planner's errors (ρ=0.85\rho=0.85) and do not help; Reacher remains negative (Abstract, Sec. 6.2, Limitations).

W2. Light formal results. Agreed. Theorem 1 is now Proposition 1 with a 3-line inline proof, the rollout bound is a cited lemma (Appendix H), and Section 3 states explicitly that learned models lack a uniform ε\varepsilon, our audit uses median residual ε^\hat\varepsilon (4%–12% misplacement among resolved candidates), and EliteCert uses no bound at deployment. We also added a 336-decision audit at 150x10 (Appendix J).

Q1. Gain as validator quality approaches the threshold; margin vs. gain. We ran a controlled sweep (Sec. 6.2, Appendix I), stopping the three retrained Push-T predictors after 1, 2, and 4 epochs as validators for the official planner (1,800 paired runs/row):

ValidatorsMargin Δq=q0.1(planner)−q0.1(val)\Delta q = q_{0.1}(\text{planner}) - q_{0.1}(\text{val})AdmittedGain vs. official (82.5%)
1 epoch-0.01No+3.9 [+2.2, +5.8]
2 epochs+0.01 to +0.02Yes+6.1 [+4.2, +8.0]
4 epochs+0.05 to +0.06Yes+7.6 [+5.6, +9.6]
Best epoch+0.07 to +0.10Yes+9.1 [+7.2, +11.1]

Within one architecture and task, gain rises monotonically with Δq\Delta q in every planner seed (gains vs. official include predictor quality; see W1). Two caveats make q0.1q_{0.1} a cautious safety filter rather than a sharp predictor:

  1. Boundary noise: Window-bootstrap 95% CIs on Δq\Delta q have half-width ±0.01–0.02\pm 0.01\text{--}0.02. The 1-epoch Push-T set (Δq≈−0.01\Delta q \approx -0.01, CIs spanning zero) still adds +3.9 pp, whereas self-trained Reacher models at Δq≈−0.01\Delta q \approx -0.01 (CIs strictly below zero) lose -6.3 [-11.0, -1.7] pp. The sentence that the test "admitted every set that helped" is withdrawn.
  2. Cross-task ordering: Δq\Delta q ignores error correlation ρ\rho—retrained Cube predictors pass widely (+0.05 to +0.14) yet add nothing because ρ=0.85\rho=0.85.

Q2. Stronger planning model shift & cheap online check. A passive monitor scored full pools without changing decisions across the 600 official Push-T tasks (Sec. 6.3, Appendix E.1):

  • Deployment & stronger planners over-cover: Fixed δ=0.481\delta=0.481 (90% target) covers 91% [89, 92] of promotions under native CEM, 93% under EliteCert, and 96%–97% when a stronger retrained predictor plans (fewer promotions, closer to the cut-off).
  • Larger search budgets under-cover: At 300x30, coverage drops to 84% overall (73% at iteration 29); recalibration gives δ=0.657\delta=0.657 (90% coverage), used in our 95.4% default-budget run.
  • Cheap online check: Using model evaluations only, calibrating δ\delta on 20 monitored tasks gives 0.45±0.100.45 \pm 0.10 and covers 89±4%89 \pm 4\% of promotions on the remaining 580 tasks.

Q3. Estimating ε^\hat\varepsilon and δ\delta online from small subsets.

  • Band δ\delta: Yes—20 tasks suffice with model evaluations alone (Q2).
  • Residual ε^\hat\varepsilon: Needs true outcomes from a resettable simulator (unavailable on hardware). In simulation, 20 decisions ×\times 50 candidates/pool (1,000 rollouts/iteration vs. 168,300 full) estimates late ε^\hat\varepsilon within +4±6%+4 \pm 6\% and resolved fraction at 0.27 [0.25, 0.30] vs. 0.28 (App. E.1). EliteCert does not use ε^\hat\varepsilon at deployment.

Comments on the paper

3 comments

Dear authors and reviewers,

The author-reviewer discussion period closes on November 18 (AoE). Please engage in response periods so that we have our issues discussed thoroughly.

AC

I believe the authors could provide answers to some of the questions first, which would help the reviewers with further assessment.

We thank all three reviewers for their constructive feedback. Two reviews noted that the submitted draft was hard to follow, and we agree that dense, inconsistent exposition obscured both the problem and the method. We rewrote the main text for clarity and ran 17 new follow-up experiments answering every reviewer question—plus stronger single-model and compute-matched baselines that sharpen how our results should be read.

1. Disentangling single-model quality from ensemble re-scoring (new baselines). The submission compared EliteCert (official planning model + 3 public checkpoints as validators) against the official model alone, without running each validator alone as a planning model under the official protocol. Evaluating each public checkpoint alone (Push-T, 600 tasks ×\times 3 planner seeds = 1,800 paired runs/cell, 95% task-cluster bootstrap CIs) yields:

Planner, budgetOfficial aloneBest single aloneEliteCertvs. Officialvs. Best single
CEM, 150x1082.588.991.2+8.7 [+6.8, +10.5]+2.3 [+0.7, +3.8]
CEM, 300x30 (default)87.493.295.4+8.0 [+6.2, +9.9]+2.2 [+0.9, +3.6]
MPPI, 150x1063.969.777.7+13.8 [+11.2, +16.3]+7.9 [+5.5, +10.4]
iCEM, 150x1066.178.978.5+12.4 [+9.9, +15.0]-0.4 [-2.8, +1.9]
  • Upgrade the single model first: Each public checkpoint alone beats the official Push-T model by +4 to +13 pp—and a single predictor retrained on the official frozen encoder reaches 89.3% with CEM—at zero extra planning cost.
  • What independent re-scoring adds on top: Over the strongest single model for each planner, EliteCert adds +2.3 pp with CEM at 150x10, +2.2 pp at the saturated default 300x30 budget (reaching 95.4%), and +7.9 pp with MPPI, while matching the best single model on iCEM (-0.4 pp).
  • Updated claims: Abstract, Intro, Table 2, and Section 6 now report every gain against both baselines. Two overbroad claims are withdrawn: (i) beating default 300x30 in half the CPU time holds against the official model (91.2% vs. 87.4%), whereas the best single model at 300x30 (93.2%, gaining +4.3 pp from extra search) exceeds the 150x10 ensemble by 2.0 [+0.3, +3.7] pp; (ii) on a laptop GPU, small validator batches make 150x10 EliteCert slower than native 300x30 (2.38 s vs. 1.90 s/decision), so speedup claims apply to CPU only.

2. Core diagnostic & mechanism findings.

  • Why search saturates (Sec. 4, App. J): Executing all candidates across 561 decisions at 300x30 shows predicted-vs.-true rank correlation falling from 0.63 to 0.23 (corrected in the Abstract from 0.74 on a 70-decision subset). A new 336-decision audit at 150x10 confirms this drop within 10 iterations (0.63 to 0.48) and shows band elites reach the goal more often than native elites (45.1% vs. 40.4%, +4.7 [+3.7, +5.7] pp late in search).
  • Error independence (ρ\rho) governs transfer (Sec. 5, 6.2): MC-dropout copies add nothing significant (+1.0 [-0.4, +2.4] pp) because their cost-difference errors correlate with the planner at 0.93–0.97 at 150x10, vs. 0.72–0.83 for independent models (0.71 vs. 0.54 late at 300x30; both are now reported). Shared-encoder retraining helps on Push-T (ρ=0.54\rho=0.54, +9.1 pp) but fails on Cube (ρ=0.85\rho=0.85, 0.0/+1.5 pp), where an independent-encoder validator (ρ=0.58\rho=0.58) adds +2.9 pp.
  • MPPI gain is re-ranking, not cost scaling (Sec. 6.1, reply to HGJE): Controlled arms show elite ordering alone recovers 89% of MPPI's gain (+12.3 pp); cost-spread compression alone adds -0.2 pp.
  • Role of the band (Sec. 6.1): Full-pool re-scoring beats the band by +1.2 [+0.1, +2.3] pp at 2.9x validator rollouts, while at matched total rollouts a smaller fully re-scored pool (80x10, 90.2%) matches the band (-0.9 [-2.4, +0.5] pp). Thus, independent re-ranking drives the gain while the band caps validator cost for a fixed pool. Calibrated widths 0.296 and 0.481 do not differ (-0.3 [-1.3, +0.8] pp; the broader 0.1–1.0 insensitivity claim is removed).

3. Presentation & reproducibility. Section 2 names all planners, shows one iteration (Figure 1), and defines each term once (Table 1; costs are minimized, elites are the KK lowest-cost sequences). Proposition 1 has a 3-line inline proof, and diagnostic counts are called "empirically resolved" rather than "certified." Tasks, metrics, baselines, and main results (Tables 2–4) are all in the main text, and run-to-run trajectory variation (~1 in 50–100 tasks, captured by our task-cluster bootstrap CIs) is quantified in Appendix C alongside our anonymized supplementary code package.

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