acceptodds
Under review as a conference paper at ICLR 2027

CERES: Capability-Aware Fast-Slow Underwater Navigation with Corrective Experts

Abstract

Robots operating with heterogeneous sensing face two coupled deployment decisions: whether a responsive default policy remains inside its capability envelope and, when correction is valuable, which control variable additional computation should revise. Degraded representations, unsafe current actions, and persistent plan failures demand distinct authority and effect times. We present CERES (Capability-Envelope Routing with Expert Specialization), a fast–slow controller that turns these decisions into cost-aware selection among causally typed interventions. System 1 continuously provides a bounded proposal and competence evidence; a coordinator combines learned correction value, realized-outcome memory, and an admissibility contract to preserve fast control or invoke System 2. System 2 centers on two current-decision experts: a State Refiner repairs the representation and a Safety Verifier certifies or projects the action; a Capability Planner conditionally extends correction to subsequent context under verified delayed execution. Across 72 paired trials in three underwater scenes, CERES preserves all 48 routine System 1 successes while recovering 14/24 challenging trials, reaching 86.1% overall success versus 66.7% for System 1 and 72.2% for always-on System 2. It reduces System 1 collision from 16.7% to 1.4% and always-on normalized expert-forward load by 39.5%. At matched success with a near-always-on risk rule, CERES uses 29.6% fewer active experts per decision. Targeted evaluations establish strong representation repair, complementary action-risk correction, verified delayed planning semantics, and a complete fast path below 50 ms at P99.

Primary area:
applications to robotics, autonomy, planning
Keywords:
robot learning, adaptive computation, fast-slow control, expert routing, multimodal perception, underwater robotics, safe robot control

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_1hQ1OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper presents CERES, a fast–slow controller for multimodal underwater navigation that selectively augments a frozen reactive policy with corrective experts. Its central contributions are a cost-aware router, trained using matched short-horizon continuations and informed by realized-outcome memory, and an intervention framework that assigns experts distinct write targets and execution times: the State Refiner repairs the current representation, the Safety Verifier projects the current action onto a learned feasible set, and the Capability Planner revises subsequent decision context. An admissibility contract constrains expert selection and execution. Evaluation comprises 72 paired trials across three simulated underwater scenes, supplemented by router comparisons, expert ablations, targeted mechanism studies, adapted VLA baselines, and latency measurements. CERES achieves 86.1% success, compared with 66.7% for the reactive policy and 72.2% for always-on correction, while reducing normalized expert-forward load by 39.5% relative to always-on correction. The results provide evidence for selective correction, with the strongest mechanism-specific gains coming from representation repair.

Critical strengths
  1. a useful formulation of selective correction
    CERES distinguishes interventions by both their modification target and their time of effect, separating representation repair, current-action correction, and subsequent-context revision. This makes the allocation problem more concrete than simply deciding whether to invoke additional computation and provides an interpretable structure for studying heterogeneous controller failures.

  2. meaningful system-level improvements with paired evaluation
    Across 72 paired trials, CERES improves success from 48/72 for System 1 and 52/72 for always-on correction to 62/72, preserving all 48 routine-task successes. Representation repair also produces a substantial targeted improvement, from 0/16 to 14/16 successes. These results support the practical value of selective correction in the evaluated simulation setting.

Critical weaknesses
  1. The evaluation does not capture the closed-loop consequences of corrective computation latency.
    Simulation pauses during policy inference, whereas expert decisions average 203.81 ms and reach 470.10 ms at P99 against a 50 ms simulation increment. Expert intervention is frequent, with an episode-averaged duty of 64.4%. Consequently, the reported success and safety results exclude motion and observation staleness during deliberation. Fast-path latency below 50 ms therefore does not establish responsiveness of the complete deployed controller.

  2. The evidence insufficiently isolates the central routing and intervention-design contributions.
    With the same corrective stack, risk rules match CERES at 62/72 successes and achieve numerically higher progress and SPL. CERES reduces calls per decision by 29.6%, but total expert forwards by only 6.3%; neither metric directly establishes end-to-end computational savings. Fixed-threshold comparisons also leave the performance–cost trade-off incompletely characterized. Evidence for planning and expert composition is limited: adding CP improves targeted success from 5/16 to 6/16, while adding SV to SR reduces state-and-safety success from 87.5% to 50.0%.

Questions for authors

Four parts of questions are as follows, looking forward to receiving your rebuttals:

  1. During the 200–470 ms expert computation period, what action would the deployed controller execute? Is there existing evaluation in which physics continues during inference or measured inference delays are explicitly injected?

  2. How were the rule-based and uncertainty-routing thresholds selected? Are end-to-end computation measurements available for these controls and CERES, including routing, memory retrieval, diagnostic forwards, and System 1 recomputation?

  3. What explains the substantial deterioration when SV is added to SR on the state-and-safety tasks? Do existing trajectory analyses distinguish conservative safety intervention from expert incompatibility or coordination failure?

  4. How are SV constraint targets, CP revision/subgoal targets, and matched continuation labels generated? Please specify the continuation horizon, subsequent control policy, and whether labels are refreshed as the experts change during coordinated optimization.

2 comments
AuthorsOpenReview ↗

Response to Reviewer 1hQ1: Closed-Loop Latency, Routing Isolation, and Training Protocol

Thank you for recognizing the selective-correction formulation and paired evidence. We answer the four questions with additional trace analyses and post-submission diagnostics.

1. Closed-loop latency. In the submitted evaluation, simulation time pauses during inference; hence no physical command is executed during the reported 200--470 ms. We agree that P99 < 50 ms describes the complete fast path, not expert decisions.

We additionally injected the measured CUDA-synchronized delays while physics advanced at 20 Hz. A conservative 72-trial test that holds for every missed deadline remained collision-free (0/72 collisions), but achieved 48/72 successes, showing that holding alone is overly conservative. We therefore tested an event-driven policy: while correction is pending, the latest completed correction is executed only after revalidation against the fresh observation; otherwise the controller holds. Results are timestamped, stale corrections are rejected, and CP remains next-decision-only. On a post-submission diagnostic panel of 10 challenging trials, this policy achieved 10/10 successes and 0 collisions while rejecting 148 stale commits. We will identify this as a diagnostic panel, not a replacement for the registered 72 trials.

2. Thresholds, computation, and routing isolation. The uncertainty threshold (0.5) and risk thresholds (0.5/0.75) were frozen before the 72 outcomes and were not selected on Paper72. Uncertainty routing selects M0 below 0.5 and M5 otherwise. Risk routing uses uncertainty, cross-modal conflict, anomaly, and failure evidence to select a legal typed configuration under the same contract.

CERES timing is observation-ready to final action with CUDA synchronization; it includes diagnostics, routing, memory retrieval, System-1 computation/recomputation, selected experts, and aggregation. Alternative-router traces were not collected under the same fixed-load timing benchmark, so we use completed expert forwards rather than present their wall-clock times as directly comparable.

We also ran three causal temporal-randomization controls that do not inherit CERES's realized per-trial configuration multiset. They obtained 60/72, 61/72, and 61/72 successes using 40,549, 38,221, and 38,852 forwards, versus CERES's 62/72 with 31,619. CERES therefore used 17.3--22.0% fewer forwards while preserving or improving success. Together with the risk-rule result (both 62/72; 33,739 versus 31,619 forwards), this supports more efficient intervention allocation at matched success. System-level capability improvement is established separately by the paired System-1 and always-on controls.

3. SR+SV deterioration. Trace attribution distinguishes conservative intervention from expert incompatibility. On state-and-safety trials, SR achieves 14/16 and SR+SV 8/16. All six discordant losses are timeouts, not collisions. SR+SV produces 6,377 safe holds, of which 6,356 result from an empty predicted SV feasible set. Thus the mechanism is conservative empty-set handling under combined difficulty, rather than destructive overrides or CP same-decision feedback. This also explains why configuration selection matters: on action-risk trials, SV improves success from 0/16 to 7/16 and removes five collision episodes, but it should not be invoked indiscriminately after representation repair.

4. Targets and continuation protocol. SV targets are generated from the same causal snapshot and candidate action: current safety, next-step veto, risks at horizons {1,5,10,20}, the linear feasible set from the geometric/kinematic certificate, and the exact projected action. CP separately supervises a causal revision event, a graph-legal successor, and a valid local subgoal in the observed body frame; a proposal at t first affects context at t+1.

Router labels use 20-step matched continuations for the fast path and every legal configuration. Each branch starts from the identical simulator/controller state, history, RNG state, and disturbance schedule; its configuration is fixed throughout the continuation, with fresh causal observations regenerated each step. Labels are frozen before the 12-epoch coordinated stage and are not regenerated as parameters update, avoiding a moving target. SV and CP continue receiving their fixed geometric and graph-structured targets during the low-learning-rate updates.

We will incorporate these clarifications, attribution results, and appropriately scoped latency diagnostics in the revision.

Area_Chair_6NPwOpenReview ↗

Reviewer 1hQ1 please respond to author comments

Reviewer 1hQ1 please respond to author comments

Reviewer_yhzEOpenReview ↗
Rating
1
Confidence
4
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The proposed CERES, a fast and slow controller for underwater navigation. A frozen reactive policy runs by default and outputs uncertainty, inconsistency, and failure diagnostics. A learned coordinator then decides at each step whether to keep the System 1 action or to call one of five allowed combinations of three System 2 “experts”. The first expert is a State Refiner, which corrects the latent representation and recomputes the System 1 action. The second is a Safety Verifier which projects the action onto a learned linear feasible set (Eq. 4). The third is a Capability Planner which revises the subgoal or capability for the next decision. The router is trained on counterfactual short-horizon rollouts of every configuration, all started from the same simulator state. The utility used for training balances completion, progress, collision, and the number of experts used (Eq. 3). The router also includes a hand-designed admissibility check (Alg. 1) and a realized outcome memory.

Critical strengths

Explicit typing of interventions. The paper separates three kinds of corrections: corrections that rewrite the representation correction that override the current action, and corrections that only change the context of the next decision. Each has a fixed execution order and timing. I find this separation useful. It makes the system auditable, and it makes the expert removal ablations meaningful, since removing one expert removes exactly one write path.

All controllers share the same seeds, initial states, disturbance schedules, and memory initialization. Every trial is kept in the analysis, and the authors use McNemar and permutation tests with Holm correction. Within its scope, this protocol is cleaner than in most robot learning papers.

Critical weaknesses

No comparison with, or positioning against, existing underwater navigation methods. The paper presents itself as underwater navigation with VLA style and fast and slow control. However, the only underwater navigation work cited is Yang et al. (2023), which appears in the Introduction and in the first paragraph of Related Work. Recent underwater work that uses foundation models or hierarchical designs with slow reasoning and fast control is not discussed. This includes UnderwaterVLA (Wang et al., 2025), a “dual brain” VLA that separates high level reasoning from reactive control; USIM/U0 (Gu et al., 2025), an underwater-specific VLA and dataset with obstacle avoidance navigation; frameworks that combine a VLM planner with a local planner, such as DREAM (Wu et al., 2025) and CORAL (Wu et al., 2026); and earlier learned goal conditioned underwater navigation (Manderson et al., RSS 2020). The paper never explains how CERES differs from or improves on these designs. Therefore, it is hard to judge the novelty of the work in this domain.

No underwater navigation baselines or established benchmark. Every baseline is either an internal variant of CERES or a generic VLA that is not designed for underwater use (OpenVLA, SmolVLA, Octo, SpatialVLA, X VLA, π0, π0.5). No existing underwater navigation method is evaluated, and no underwater-specific VLA such as U0 is included. There is also no classical baseline, such as a local planne combined with a safety filter, even though CERES already uses an occupancy map and a range scan as inputs. Furthermore, the tasks are three custom Isaac Sim scenes instead of an established underwater simulator or benchmark. As a result, the numbers cannot be compared with any prior published result.

Simulation only, with no real-world experiments. All results come from Isaac Sim. No real vehicle, tank, or real sonar data is used. I have three concerns here. First of all, the sensor degradation is synthetic, and SR is supervised to recover the clean representation under “known observation degradation” . So the state degradation tests likely come from the same degradation family that SR was trained on.Secondly, router supervision requires resetting the simulator and rolling out all six configurations from identical states (Eq. 3; Alg. 3). This kind of supervision cannot be collected on a real vehicle. Last but no least, hydrodynamics, currents, and sonar simulation are not described, and control is a planar 2D (v, ω) command. The paper does not discuss sim-to-real transfer.

The VLA comparison is confounded by unequal inputs and training budgets. Inputs. CERES uses RGB, sonar, point cloud, proprioception, occupancy, and range scan. The VLAs only receive “current RGB, task text, and the same causal body frame goal”, and SmolVLA also receives proprioception. The authors themselves note that CERES keeps its complete onboard interface while the external policies use only their supported native inputs.

Training. All methods use the same 700 training episodes. However, the VLAs with native adaptation see 11,200 anchor samples, which is about 6% of the 198,721 frames used to train CERES, for 700 steps at batch size 16 with a single seed. The frozen backbone variants only fit a ridge regressor on 2,800 samples. In contrast, CERES components are trained for 8 to 30 epochs over the full set of frames. Therefore, the gaps of 53 to 83 points in Table 3 mostly reflect differences in input modalities and training budget, not the value of capability-aware routing. A fair test would give the VLAs the same sensors, use a matched data budget, or compare against an underwater-specific VLA.

Questions for authors

How does CERES differ conceptually from existing underwater navigators with fast and slow or hierarchical foundation model designs, such as the dual brain design of UnderwaterVLA, or frameworks that pair a VLM planner with a local planner and replan when verification fails? Can you evaluate against at least one underwater navigation method, and against a classical planner with a safety filter that uses the same occupancy and range inputs? Can you compare against an underwater-specific VLA such as U0, or give the generic VLAs the same sonar and range inputs and a matched training budget? Is any real-world or tank validation possible? If not, how would router supervision, which needs counterfactual rollouts from identical states, be obtained on a real vehicle? How are hydrodynamics and sonar simulated? Are the state degradation test conditions drawn from the same degradation family used to train SR? Can you report results on held-out degradation types? What happens if simulation time is not paused during policy computation? How many independent training seeds were run? Please report the variance for Tables 1 and 2.

2 comments
AuthorsOpenReview ↗

Response to Reviewer yhzE: New Matched Evidence and Underwater Positioning

Thank you for the detailed review. We have completed additional matched experiments addressing the central empirical concerns; the new evidence strengthens the paper's main conclusion.

1. Relation to underwater systems. UnderwaterVLA separates foundation-model reasoning from hydrodynamics-informed MPC; DREAM/CORAL select semantic goals or waypoints for local planners; U0 learns a general underwater VLA; and Nav2Goal learns goal-conditioned visual navigation. CERES addresses an orthogonal closed-loop question: given a default proposal, whether correction is warranted and which variable it may modify. SR repairs the current representation, SV verifies/projects the current action, and CP revises only subsequent context, with constrained write authority, ordering, and effect time. CERES therefore governs mechanism-specific corrective authority inside the control loop rather than implementing another high-level/low-level hierarchy. We will add this positioning.

2. Matched VLA training budget. The submitted native adaptations used 11,200 episode-balanced anchors, whereas CERES used 198,721 frames. We retrained SmolVLA and Octo using all 198,721 unique causal frames from the same 700 episodes (12,421 optimizer steps; effective batch 16), selected on Dev100 only, and evaluated once on untouched Paper72. SmolVLA obtains 13/72 successes (1/24 challenging), Octo 18/72 (0/24), and CERES 62/72 (14/24). Thus the capability gap persists under the complete training-frame budget, ruling out insufficient adaptation data as its explanation for these two native policies.

The external policies retain their supported native interfaces, because adding CERES-specific sonar/point encoders would create new architectures rather than evaluate the published policies. We use this as whole-policy evidence; mechanism attribution rests on matched internal controls sharing observations, experts, tasks, safeguards, and execution contracts.

3. Unseen degradation operators. We audited the frozen targeted population by operator identity without outcome-based selection. Five tested families were absent from SR training: contrast attenuation with depth fog, regional RGB masking, sonar range noise, point-cloud outliers, and localization bias. SR-directed control succeeds in 9/10 held-out trials versus 0/10 without SR (two-sided exact paired p=.0039); across all targeted degradation trials, it achieves 14/16 versus 0/16. This directly rejects the interpretation that SR succeeds only by inverting its training degradations.

4. Multi-seed stability. We trained two additional independent Stage-4 checkpoints, changing initialization/data order while keeping frozen data and hyperparameters fixed, and evaluated each on all 72 tasks. With the submitted checkpoint, success is 62/72, 60/72, and 59/72 (83.8% mean; 2.1-percentage-point sample SD), collisions are 1, 2, and 1, and mean progress is .5435, .5451, and .5431. End-to-end performance is stable across the three independently trained router/memory and SV/CP/aggregation instances.

5. Classical control. We evaluated observed-map A* with a causal safety filter on the same 72 initial states, occupancy/range observations, action limits, disturbances, and termination rules. It obtains 60/72 successes, zero collisions, progress .618, and SPL .796; CERES obtains 62/72, one collision, progress .544, and SPL .802. This establishes a competitive comparison with a strong geometry-based controller, while CERES additionally provides cross-modal representation repair, learned action verification, delayed context revision, and outcome-conditioned selection among these interventions.

6. Simulation and deployment scope. Evaluation uses three-dimensional Isaac Sim scenes, multimodal sensing, bounded lateral-current disturbances (0.10/0.18 m/s), sonar dropout/range corruption, and planar body-frame commands. Counterfactual continuations generate supervision offline; deployment uses only causal observations and realized past outcomes, requiring neither physical resets nor online counterfactual rollouts. We will state clearly that tank/field validation is outside the current evaluation.

The 50-ms value is the physics integration interval. Ready-observation-to-action P99 is 45.23 ms for the complete fast path and 470.10 ms for expert decisions. Since the submitted simulator pauses during inference, we will describe this as fast-path responsiveness, not a 20-Hz guarantee for every corrective decision.

The new evidence removes the VLA training-budget explanation, demonstrates significant transfer to unseen degradations, establishes multi-seed stability, and supplies the requested matched classical control. We hope the reviewer will reconsider the soundness assessment in light of these results.

Reviewer_yhzEOpenReview ↗

Partially addressed my concern but I retain my score

From both a learning perspective and a robotics perspective, most of my concerns are not addressed. There needs to be a strong baseline. I want to see it compared to other dual-brain models. U0 is not evaluated, which is closer to your work. There is no established benchmark. The method that is being compared has different input, which is an unfair comparison. What is hydrodynamics being used and the sonar? How is it the same in the real world? There will be a huge domain gap. This is in simulation where you can pause time, but in real life, you really cannot. Echoing back to the hydrodynamics, the robot itself would also move, and it might not move as you expect in real water.

Reviewer_12XJOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

This paper proposes CERES, a fast-and-slow controller for underwater robot navigation. A learned coordinator decides at each step whether to execute a frozen reactive policy which is System 1 or to invoke a legal configuration of three corrective experts which is System 2 policy. The main contributions are the formulation of fast-slow coordination as cost-aware selection and a mechanism-specialized System 2 consisting of a State Refiner, a Safety Verifier, and a Capability Planner with constrained composition and ordering. The coordinator is trained from short-horizon counterfactual continuations under a utility that rewards progress and penalizes collision and expert count, and it additionally conditions on a memory of realized outcomes. The authors validate the approach in Isaac Sim and perform many other ablations.

Critical strengths
  1. The protocol and eval is unusually rigorous for a robotics systems paper. The authors have done a great job with paired tests and all statistically significant numbers.

  2. The result that CERES preserves all 48 routine System 1 successes while always-on System 2 loses 8 of them (in Table 1, Table 9) is a nice demonstration of the paper's central premise. This is generally the half of the fast-slow claim that is most often asserted and least often shown, and I believe it is shown convincingly here.

Critical weaknesses

The paper attributes its ~13.9 pp advantage over always-on System 2 to capability-envelope routing, but the decomposition in Table 9 shows that 8pp come from always-on System 2 failing routine tasks that System 1 solves, and only 2 trials (14 vs 12/24) come from the challenging stratum where the experts are supposed to add value. The paper does not explain why always-on System 2 degrades routine performance. Because the authors describe SV as having 'final learned authority over the current command" whenever it is active, I am wondering whether the experts, and SV in particular, are actively harmful when invoked on a competent proposal, in which case the contribution is better described as "gating protects the fast policy from the experts" than as "typed experts recover lost capability."

Additionally, Appendix D, Table 12 reports a diagnostic that shuffles CERES's own realized per-trial configuration multiset in time, and this diagnostic achieves 64/72 against CERES's 62/72 with fewer total expert forwards (30k vs 31k). The authors do not discuss it in the main text. However, if random temporal placement of the same intervention budget matches or exceeds the learned router, then the learned when to intervene decision, which is the paper's first stated contribution, is not demonstrated to carry value beyond controlling the overall intervention rate. Given that the deployable risk-rule router also matches CERES on success and differs by only 6.3% in total forwards, the evidence for the learned coordinator reduces to a modest compute saving rather than a capability gain, which is a substantially weaker claim than the one made in the abstract and introduction.

Questions for authors
  1. Which expert is responsible for the 8 routine failures under always-on System 2? This would improve the paper and per-expert attribution on those 8 trials would resolve whether the experts are harmful when unnecessary.
  2. How do the authors interpret the frozen-distribution diagnostic outperforming CERES? in other words, is there a reason it should not be read as evidence that temporal placement is unimportant?
  3. Why does SR+SV+CP underperform SV+CP and SR+SV in the all-mechanisms class (Table 14)?
  4. Were the router and experts trained with more than one seed? It would help to report this in the paper.
3 comments
AuthorsOpenReview ↗

Response to Reviewer 12XJ: Expert Attribution and Routing Controls

Thank you for the careful analysis. Our follow-up diagnostics sharpen and strengthen CERES's central result: corrective experts recover capability on difficult cases, while selective configuration prevents unnecessary correction from degrading competent behavior.

1. Which expert causes the eight routine failures? All eight trials are completed by System 1 and CERES but time out under always-on System 2; none collides. Trace attribution finds 6,788 safe holds: 6,776 arise from SV predicting an empty feasible-action set and 12 from actuator-preview rejection. We replayed exactly these eight trials under every fixed legal configuration. Success decreases from 8/8 for M0 to 7/8 for SR, 5/8 for SV, 3/8 for SR+SV, 2/8 for SV+CP, and 1/8 for SR+SV+CP; all remain collision-free. Safe holds increase from 0 for M0/SR to 3,489, 4,643, 5,547, and 6,316 for the four SV-containing configurations. Thus conservative SV-mediated final-action authority, compounded by unnecessary expert composition, causes the routine timeouts.

This does not indicate that SV is generally harmful. System 1 completes 0/24 challenging tasks, whereas always-on System 2 completes 12/24 and CERES 14/24. In targeted action-risk trials, SV raises success from 0/16 to 7/16 and removes five collisions. Together, these results demonstrate the central premise: corrective authority recovers capability when needed, while selective routing protects already competent proposals.

2. Frozen-distribution diagnostic and learned routing. The submitted frozen-distribution row is an outcome-informed diagnostic, not a deployable router: it inherits CERES's realized per-trial configuration multiset and then shuffles its timing. Its 64/72 therefore does not show that an online policy can reproduce this result from causal observations.

We ran two stricter controls. A temporal shuffle that does not inherit CERES's realized per-trial intervention multiset obtains 60/72, 61/72, and 61/72 across three seeds, versus CERES's 62/72, while requiring 40,549, 38,221, and 38,852 expert forwards versus 31,619 for CERES (17--22% fewer). Deployable i.i.d. causal routing obtains 63/72, 61/72, and 62/72 but requires 41,262--45,889 forwards; CERES therefore uses 23--31% fewer forwards at comparable success. These results directly contradict the interpretation that CERES merely controls the overall intervention rate: it provides observation-conditioned allocation with substantially lower corrective computation than non-learned temporal controls. We will clarify that matched-control success differences are not statistically significant; the isolated routing contribution is lower computation at matched effectiveness, while the system-level capability gain comes from selective typed correction under the shared admissibility contract.

3. Why is the full expert set not always best? The experts have different write targets and are not intended to improve monotonically when stacked. In the 16 all-mechanisms trials, SR+SV, SV+CP, and SR+SV+CP obtain 6/16, 7/16, and 5/16 successes, all with zero collisions. The full configuration produces 4,120 safe holds versus 3,837 and 3,457; over 98% arise from empty SV feasible sets, producing conservative timeouts. CP still satisfies its causal contract: its revision first affects the next decision. This non-monotonic composition directly motivates selecting among typed legal configurations instead of invoking every expert.

4. Training seeds. The submitted checkpoint used one optimization seed. We trained two additional independent Stage-4 checkpoints (router/memory and SV/CP/aggregation; identical frozen data and hyperparameters) and evaluated each on all 72 tasks. Together with the submitted checkpoint, success is 62/72, 60/72, and 59/72 (83.8% mean; 2.1-percentage-point sample SD), collisions are 1, 2, and 1, and mean progress is .5435, .5451, and .5431. Thus end-to-end outcomes are stable across the three independently trained Stage-4 instances.

The new causal attribution, stricter routing controls, and three-seed end-to-end evaluation support three distinct conclusions: typed correction provides mechanism-specific recovery; admissibility enforces legal composition; and learned routing provides causal, deployable allocation with lower corrective computation at matched effectiveness. We hope these results address the reviewer's concerns regarding the coordinator and expert composition.

Area_Chair_6NPwOpenReview ↗

Reviewer 12XJ please respond to author comments

Reviewer 12XJ please respond to author comments

Dear author(s), thanks for the rebuttal and additional details, they partly address my questions and strengthen the paper. I would like to maintain my score, this is because the new results (and the original paper) confirm that much of CERES's advantage over always-on System 2 comes from avoiding harmful expert interventions. Although the additional controls provide stronger evidence for computational efficiency, my main concern about the contribution of the learned coordinator remains. This is a fundamental fix that would require a change in the method itself.

All the best!

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

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