acceptodds
Under review as a conference paper at ICLR 2027

Brain-Inspired Prior Regulation for Efficient Planning with World Models

Abstract

Advances in world models enable predictive reasoning about action consequences, supporting goal-directed decision-making in robotic manipulation and visual navigation. However, action search remains computationally expensive, and existing prior-guided methods improve sampling efficiency through initialization but lack persistent regulation of subsequent optimization, leaving search vulnerable to deviations from the learned action prior. To address this limitation, we propose Brain-Inspired Prior Regulation (BIPR), a framework for efficient planning with world models through coordinated prior regulation across multiple timescales. Specifically, prior anchoring penalizes deviations from the action prior throughout search, uncertainty–conflict arbitration adapts regularization to current search evidence, and metaplastic calibration uses offline learning history to modulate this adaptive response. Experiments on established benchmarks for world-model-based control show that BIPR improves macro-average success rates with LeWorldModel and Sub-JEPA by 30.33 and 26.33 percentage points, respectively, over the MPPI baseline, while complementary efficiency evaluations demonstrate a 46.73% reduction in evaluation wall time relative to CEM under a matched candidate budget. Beyond task success, computational cost analysis shows that BIPR requires no additional trainable parameters compared with prior-guided planning, while incurring only 0.82% additional evaluation overhead. These findings suggest that brain-inspired prior regulation offers a promising approach to improving the performance–efficiency trade-off of world-model-based planning.

Primary area:
applications to robotics, autonomy, planning
Keywords:
World Models, Brain-Inspired Planning, Action-Prior Regularization

Reviews

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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.
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Paper summary

This paper proposes Brain-Inspired Prior Regulation (BIPR) for improving sampling-based planning with learned world models. The main motivation is that existing prior-guided planners such as PRISM use an action prior mainly to initialize the search distribution, but subsequent optimization can drift away from prior-supported actions. BIPR addresses this with three mechanisms: Prior Anchoring, which continuously penalizes deviations from the learned action prior; Uncertainty–Conflict Arbitration, which adaptively adjusts the regularization strength based on prior spread and disagreement between model-preferred candidates and the prior; and Metaplastic Calibration, which further modulates this response using prior-head training progress. The method reuses the same candidate rollouts and adds no trainable parameters beyond the shared prior head.

The paper evaluates BIPR on four control environments using frozen LeWorldModel and Sub-JEPA backbones. BIPR improves average success over MPPI by 30.33 and 26.33 percentage points, and over the more directly comparable PRISM baseline by 8.00 and 4.83 points, respectively. The paper also reports ablations, runtime comparisons, sensitivity studies, and qualitative rollouts.

Critical strengths
  1. Persistent prior regulation addresses a concrete weakness of prior-guided planning. The main idea of extending action-prior guidance from initialization to candidate scoring throughout optimization is simple but meaningful. The ablation suggests that Prior Anchoring is the dominant source of improvement: on PushT and Reacher, adding Prior Anchoring improves the average success from 68.67% to 75.67%. This supports the central hypothesis that search drift after prior-guided initialization is a real problem.
  2. The method provides a favorable performance–compute trade-off with little additional online overhead. BIPR reuses the same world-model rollouts, introduces no additional trainable parameters over the shared prior-guided baseline, and increases evaluation time only slightly relative to PRISM. The evaluation also covers two predictive backbones and four tasks, which provides some evidence that the core regularization idea is not tied to a single world model.
Critical weaknesses
  1. The evidence does not cleanly support the contribution claimed for the full BIPR method. The headline improvements of 30.33/26.33 points are measured against MPPI, but most of this improvement already comes from introducing the learned prior used by PRISM. The more informative comparison for isolating BIPR's contribution is PRISM, where the gains are 8.00 and 4.83 points. Moreover, the component ablation shows that Prior Anchoring accounts for most of the improvement, while Metaplastic Calibration contributes only 0.67 points on the two evaluated tasks. Therefore, the current presentation overstates how strongly the experiments validate all three proposed components.

  2. The adaptive mechanisms are heuristic and are not sufficiently validated mechanistically. UCA uses the predicted prior variance as an uncertainty signal even though the paper explicitly notes that it is not a calibrated estimate of epistemic uncertainty. Metaplastic Calibration further uses a hard binary gate based on fixed training-progress thresholds, but the rationale for this non-monotonic rule is unclear. More importantly, the paper does not report the actual distributions or trajectories of the key internal quantities such as search drift, uu, vjv_j, or λj\lambda_j. This makes it difficult to verify that the proposed adaptive mechanisms operate as intended rather than simply acting as tuned heuristics.

Questions for authors
  1. Could the authors report the actual values of Linit,Lbest,qL_{\text{init}}, L_{\text{best}}, q, and the resulting binary gate b(q)b(q) for each environment and backbone? Since Metaplastic Calibration depends directly on these quantities, this information is necessary to understand when the module actually changes the planner behavior.
  2. How is the scale of the world-model cost CWMC_{\mathrm{WM}} calibrated relative to the prior penalty λP\lambda P across different backbones? Since the two terms are directly added and different backbones may use different latent representations or native cost aggregations, could the authors clarify whether the same λ\lambda values are robust to changes in latent-cost scale?
  3. Why does varying the conflict gain in Figure 4 appear to have no effect on performance, including at a value that should effectively remove the conflict contribution, while Table 4 reports a noticeable degradation when the conflict branch is removed? Were these experiments conducted with different seeds, protocols, or model variants?
  4. Can the authors provide a direct comparison against a simple fixed-λ\lambda prior-regularized planner, ideally using the same Gaussian prior and candidate scoring but without UCA and Metaplastic Calibration? This would help determine whether the adaptive mechanisms provide a meaningful advantage beyond persistent prior regularization itself.
4 comments

We thank the reviewer for recognizing the value of persistent prior regulation and BIPR’s favorable performance–compute trade-off.

W1

BIPR’s incremental contribution is supported by direct comparisons using a shared prior. The supplementary fixed λ comparisons and hard-gate ablations provide further evidence for adaptive regulation.

1. Shared-prior comparisons directly measure BIPR’s incremental contribution

PRISM and BIPR share the action prior, initialization, world model, and planning budget. In the original paper, BIPR improves over PRISM by 8.00 and 4.83 percentage points on LeWM and Sub-JEPA, respectively. Improvements over MPPI reflect the benefit of the overall method. We will explicitly distinguish these two comparisons in the revision.

2. Validation-tuned fixed λ comparisons support the incremental value of adaptive regulation

For each prior checkpoint, we independently select the fixed λ from six candidates, using 40 validation evaluations per candidate. We evaluate three independently trained LeWM priors, with 75 test starting states per prior. Results report mean ± SD across the three priors.

TaskPRISMValidation-tuned fixed λBIPR
PushT76.44 ± 3.85%80.00 ± 2.31%80.89 ± 1.54%
Reacher49.78 ± 6.16%56.00 ± 8.11%59.11 ± 2.04%

On Reacher, BIPR improves average success over the tuned fixed λ baseline by 3.11 percentage points, supporting the incremental value of adaptive regulation on this task.

3. Hard-gate ablations directly evaluate calibration

Component ablations now cover two backbones and three tasks. MC uses checkpoint learning progress to select between fixed anchoring and full arbitration. In the LeWM PushT hard-gate comparison, using the same prior checkpoint and 50 starting states for each of three evaluation seeds, the full method achieves 83.33 ± 4.16%, compared with 82.00 ± 2.00% for Prior Anchoring+UCA without calibration. This comparison supports an additional benefit from calibration’s branch selection in this configuration. We will clarify its checkpoint-level role in the revision.

W2

The supplementary controlled interventions and internal-trace diagnostics show that the regulation signals respond to prior degradation and model mismatch.

1. Prior spread and conflict signals have explicit operational meanings

Prior spread describes the dispersion of the action distribution and informs the strength of prior-scale-normalized anchoring. The conflict signal v measures the excess departure from the prior among model-preferred candidates, allowing arbitration to respond to model–prior disagreement during search.

In the controlled label-corruption experiments on LeWM PushT, increasing corruption from 0% to 25% and 50% raises prior action-prediction MSE from 0.6832 to 0.8739 and 1.3297, while the mean prior standard deviation increases from 0.7755 to 2.4792 and 3.5430. These measurements link prior degradation to the spread signal.

2. The interval gate selects regulation branches using learning progress

q measures the relative reduction in validation error from its initial value and describes checkpoint learning progress. The interval gate uses this quantity to determine whether to retain additional arbitration, without imposing a monotonic relationship between q and regulation strength.

The thresholds 0.15 and 0.30 were determined empirically during PushT development experiments, frozen before the supplementary experiments, and applied unchanged across both backbones. Inside the interval, the method retains base anchoring with λ = 0.5. Outside the interval, it retains full arbitration. MC therefore performs checkpoint-level branch selection, while UCA provides online adaptation.

3. Internal traces directly characterize regulation signals and search behavior

On LeWM Reacher, we scale only the actions supplied to the world model while keeping the executed actions unchanged.

MetricAction-input scale 0.75Action-input scale 0.50
Model prediction MSE0.29530.6774
Prior-spread signal u0.9280 ± 0.03310.9227 ± 0.0363
Conflict signal v0.0318 ± 0.01870.0425 ± 0.0212
Final weight λ0.9652 ± 0.01610.9632 ± 0.0168
Normalized search displacement from the prior1.0024 ± 0.27081.0526 ± 0.3062

Model prediction MSE is measured on the same 75 offline windows. Online quantities are first averaged over pre-success records within each evaluation environment. We then report the mean and standard deviation across the 75 environment-level averages.

Stronger model mismatch is accompanied by a higher conflict signal, supporting v’s responsiveness to changes in model–prior disagreement under controlled errors. λ is jointly determined by u and v. We will include these diagnostics, the threshold-selection procedure, and checkpoint branch records in the revision to make the mechanism’s behavior directly verifiable.

Q1

The learning progress and gate state of each checkpoint have been individually verified. The table below reports the main-comparison checkpoints used in our supplementary hard-gate evaluation, all with prior-training seed 42.

LinitL_{\mathrm{init}} denotes the initial validation MSE, and LbestL_{\mathrm{best}} denotes the lowest validation MSE over training. qq is the relative reduction in validation error, clipped to [0,1]. The gate is b(q)=1b(q)=1 when 0.15<q<0.300.15 < q < 0.30 and b(q)=0b(q)=0 otherwise.

BackboneTaskLinitL_{\mathrm{init}}LbestL_{\mathrm{best}}qqb(q)b(q)
LeWMCube1.0287230.6096500.4073720
LeWMPushT0.9457130.7797790.1754591
LeWMReacher1.0039680.9939900.0099390
LeWMTwoRoom1.0075870.9335670.0734620
Sub-JEPACube1.0259440.5405770.4730930
Sub-JEPAPushT0.9465650.7842010.1715301
Sub-JEPAReacher1.0038680.9937590.0100700
Sub-JEPATwoRoom1.0060230.9327340.0728510

For these checkpoints, both backbones use base anchoring with a fixed λ=0.5\lambda=0.5 on PushT and retain full arbitration on the other three tasks. The gate state is fixed per checkpoint, while UCA provides online weight adaptation. These records directly specify the planning branch selected by calibration on each task.

We will include this table and the checkpoint-to-result records in the revision to make the gating behavior directly verifiable and reproducible.

Q2

We retain each backbone’s native goal cost and consistently control the scale of the prior penalty. The supplementary experiments show that, under the tested temperature-compensated cost scaling, the same λ\lambda configuration maintains higher average success than PRISM across both backbones.

The prior penalty normalizes action deviations by the floored prior scale, averages over action-sequence dimensions, and is capped at 9, controlling the effects of action units and dimensionality. Both backbones use λbase=0.5\lambda_{\mathrm{base}}=0.5 and λmax=1\lambda_{\mathrm{max}}=1.

We further keep this λ\lambda configuration unchanged while multiplying both the world-model cost and MPPI temperature by 0.25 or 4. This preserves the ratio of model cost to temperature and directly tests changes in relative prior-regularization strength. All comparisons use the hard gate in Eq. 5, with three evaluation seeds and 25 starting states per seed for each condition. Results report the mean and standard deviation.

BackboneTaskScaling factorPRISMBIPR
LeWMPushT0.2578.67 ± 10.07%82.67 ± 6.11%
LeWMPushT478.67 ± 10.07%81.33 ± 6.11%
LeWMReacher0.2553.33 ± 8.33%61.33 ± 4.62%
LeWMReacher453.33 ± 8.33%57.33 ± 6.11%
Sub-JEPAPushT0.2590.67 ± 4.62%93.33 ± 6.11%
Sub-JEPAPushT490.67 ± 4.62%92.00 ± 4.00%
Sub-JEPAReacher0.2545.33 ± 2.31%54.67 ± 4.62%
Sub-JEPAReacher445.33 ± 2.31%46.67 ± 8.33%

BIPR achieves higher average success than PRISM across both backbones, both tasks, and both scaling factors, supporting the applicability of the same λ\lambda configuration under this temperature-compensated protocol. We will include the cost definitions, temperature-compensation settings, and complete scaling results in the revision.

Q3

Yes, the two experiments use different calibration variants and evaluation protocols. The success-rate plateau in Figure 4 does not imply that the conflict gain leaves planning outcomes unchanged.

Figure 4 uses the smooth calibration variant and sweeps conflict gains of 0, 2, 4, 8, and 16 on LeWM PushT and Reacher, using evaluation seed 42 and 20 starting states per task and setting. Table 4 uses the hard gate in Eq. 5, with three evaluation seeds and 50 starting states per seed. The flat curve therefore indicates unchanged aggregate success, rather than an absence of influence from the conflict branch.

To directly evaluate the conflict branch in the final method, we added a controlled hard-gate comparison that matches the prior checkpoint, evaluation starting states, planning budget, and random-seed protocol, disabling only the conflict branch. The Sub-JEPA Reacher results below report the mean and standard deviation across three evaluation seeds, each with 50 starting states.

BackboneTaskWithout conflict branchFull BIPR
Sub-JEPAReacher53.33 ± 10.26%55.33 ± 9.87%

The full method improves average success by 2.00 percentage points, supporting an incremental benefit from the conflict branch in this configuration. We will explicitly label Figure 4 as a supplementary analysis of the smooth calibration variant and report the configurations, evaluation protocols, and controlled hard-gate comparison in the revision.

Q4

As reported in our response to W1, we added a fixed λ baseline using the same Gaussian prior and candidate-scoring formulation, with UCA and MC removed, and tuned its weight on the validation set. Across three independently trained LeWM priors, BIPR achieves 59.11 ± 2.04% average success on Reacher, compared with 56.00 ± 8.11% for this baseline, supporting the incremental value of adaptive regulation beyond persistent prior regularization on this task.

Thank you for the clarifications and additional experiments. The tuned fixed-weight baseline and checkpoint gate records are helpful. However, the evidence for a consistent benefit from adaptive regulation and the progress-based gate remains limited. These concerns continue to affect my assessment, so I am maintaining my current rating at this stage.

Reviewer_EFbDOpenReview ↗
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Paper summary

BIPR augments prior-guided sampling-based planning in a frozen world model. It shares a learned Gaussian action prior and the initial mean/covariance fusion with PRISM, but continues to penalize departures from the prior during candidate evaluation. The penalty is a clipped, dimension-normalized Mahalanobis distance:

\left(\frac{a[d]-\mu_p[d]}{\widetilde\sigma_p[d]}\right)^2,9\right\}, \qquad s_{j,k}=C_{\mathrm{WM}}(a_j^{(k)})+\lambda_jP(a_j^{(k)}).$$ An uncertainty–conflict rule increases $\lambda_j$ from 0.5 toward 1 using prior spread and the excess prior penalty among candidates preferred by the world model. A checkpoint-level gate based on held-out prior-training improvement either retains that increase or returns to the fixed 0.5 anchor. Candidate weighting updates the search mean while the model, prior, and sampling covariance remain fixed. On four tasks, BIPR improves average success over PRISM by 8.0 points with LeWorldModel and approximately 4.83 points with Sub-JEPA. The larger headline improvements, 30.33 and 26.33 points, are relative to MPPI without a learned prior. Additional comparisons address CEM, planning budget, ablations, and computational cost. The proposed regulation adds no trainable parameters or world-model rollouts relative to the prior-guided baseline. The evidence most clearly supports a low-overhead benefit from persistent prior anchoring; the role and reproducibility of the checkpoint-dependent arbitration require further clarification.
Critical strengths
  1. The main comparison isolates a useful and inexpensive change to candidate scoring. PRISM and BIPR share the same prior head, Gaussian fusion, rollout budget, and frozen world model (§§3–4). The LeWM average improvement from 75.0% to 83.0% is therefore a more informative comparison than the headline improvement over prior-free MPPI. Prior Anchoring is simple to implement, and the four-task cost accounting reports only 0.82% additional evaluation wall time over PRISM with identical preparation/training cost (Table 7). A practical improvement of this size at such low marginal cost would be valuable even without a new network or a complicated planner.

  2. The evaluation includes transfer, ablations, and unfavorable regimes. The prior-guided comparison is repeated on Sub-JEPA, where the average improvement persists, while the paper reports that Cube ties and PushT decreases rather than claiming uniform gains (Table 2). Table 4 identifies anchoring as the largest incremental contribution and tests the uncertainty/conflict branches. Table 3 and Table 8 also show that increasing candidates or optimization rounds need not improve success. These results are useful evidence that search quality depends on the scoring objective, not just the number of model evaluations. The paper correctly acknowledges that prior variance is not a calibrated estimate of epistemic error and that the clipped penalty cannot distinguish saturated candidates.

Critical weaknesses
  1. The checkpoint gate is mathematically a switch between two ablations, but its experimental realization is not adequately documented. In Eq. (5), qq and b(q)=1{0.15<q<0.30}b(q)=\mathbf1\{0.15<q<0.30\} are fixed for each trained checkpoint. Therefore, for a given checkpoint,

    \begin{cases} 0.5, & b(q)=1,\\ \lambda_j^{\mathrm{UCA}}, & b(q)=0. \end{cases}$$ With identical inputs and random candidate draws, the full method is exactly Prior Anchoring alone in the first case and Prior Anchoring plus UCA in the second. This is a checkpoint-selection rule, not an additional continuously adapting online mechanism. Yet Table 4 reports a full-model PushT mean distinct from both preceding ablations, and does not give the checkpoint-specific $q$ values or explain whether training checkpoints/random draws differ across rows. Different seeds or checkpoints could explain the difference; the table alone is not proof of an implementation error. It does, however, prevent a clean interpretation of the claimed incremental metaplastic effect. There is a related configuration mismatch: Appendix C.1/Figure 4 varies a “smooth quality gain,” although the final hard-gate equation and Table 5 contain no such parameter. Tables 1 and 4 report full-model PushT success of $89.33\pm1.15$, while Table 3 at the same stated $K=128$ reports $88.67\pm5.03$. These may be distinct evaluation runs or an earlier planner variant, but they need an explicit mapping to configurations and seeds. Until the hard-gate implementation, sensitivity results, and ablation protocol are reconciled, the extra arbitration/calibration contribution is not reproducible from the manuscript.
  2. The incremental contribution beyond established prior-regularized planning is not yet convincingly isolated. Before clipping, the Gaussian penalty is a scaled negative log density of the floored prior, up to a candidate-independent constant. Persistent prior regularization is therefore a familiar control-as-inference idea; the brain-inspired framing is a design motivation rather than independent evidence of novelty. Most of the improvement in Table 4 comes from the fixed anchor. The full method should be compared with an equally tuned constant penalty under the same final configuration and held-out tuning protocol, not only the selected λbase=0.5\lambda_{\mathrm{base}}=0.5. The existing sensitivity plot is relevant, but its unexplained smooth-gate parameter makes it insufficient to settle this question for the stated algorithm.

    The proposed uncertainty and progress signals also need stronger mechanistic validation. Prior spread may indicate valid multimodality or insufficient learning, and a fixed interval of relative MSE improvement does not itself establish current prior reliability. The manuscript acknowledges part of this issue, but does not demonstrate that the gate selects appropriate regulation under controlled prior misspecification or world-model error. Finally, the 46.73% timing reduction is against CEM, whereas BIPR retains MPPI's fixed-covariance solver; it should not be attributed entirely to the new regulation. The genuinely incremental comparisons are the success gain and small overhead over PRISM. Three evaluation seeds with 50 episodes per task quantify evaluation variability, but do not establish robustness across independently trained priors/world models.

  3. No real-world experiments.

Questions for authors
  1. Resolve the gate and configuration bookkeeping. Please report LinitL_{\mathrm{init}}, LbestL_{\mathrm{best}}, qq, and b(q)b(q) for each task/backbone and each prior-training checkpoint used. Are all ablations evaluated with the same checkpoints and candidate random numbers? How should Figure 4's smooth-quality parameter and the differing PushT numbers in Tables 1/3/4 be reconciled with the final hard gate? A small configuration-to-result manifest would directly resolve the main reproducibility concern.

  2. Establish the value of adaptive regulation rather than penalty tuning. Can the authors compare the final method against a validation-tuned constant-λ\lambda anchor with the same tuning budget, and evaluate the gate across independently trained priors? Controlled degradation of the prior or world model, together with measurements of search displacement and prediction error, would test whether the uncertainty/conflict signals identify unreliable departures rather than simply enforcing more imitation. This is more diagnostic of the proposed mechanism than additional selected successful rollouts.

  3. Relevant missing planning references. The following paper and references therein bear directly on combining behavioral priors with model-based search:

    • Han Qi, Haocheng Yin, Aris Zhu, Yilun Du, and Heng Yang, Inference-Time Enhancement of Generative Robot Policies via Predictive World Modeling, IEEE Robotics and Automation Letters. 2026
4 comments

We thank the reviewer for recognizing our low-overhead improvement to candidate scoring and evaluation across backbones, and address each comment below.

W1

Your derivation of the conditional equivalence is correct. MC selects between base anchoring and PA+UCA at the checkpoint level, while UCA adjusts the weights during search. We verified the checkpoints, q values, and gate states used in the additional hard-gate main comparisons. All prior heads in the following table were trained with seed 42.

TaskLeWM qSub-JEPA qb(q)Equivalent branch of Full
Cube0.4073720.4730930PA+UCA
PushT0.1754590.1715301PA with λ=0.5
Reacher0.0099390.0100700PA+UCA
TwoRoom0.0734620.0728510PA+UCA

Within each additional comparison, we fix the checkpoint, test starts, planning budget, and random-number generation protocol. Strictly equivalent policies share the same verified evaluation records, with reuse explicitly marked and no additional independent repetitions counted. In the revision, we will report the calibration contribution using these comparisons under a unified protocol and provide the mapping between configurations and results.

The quality gain in Figure 4 controls a continuous calibration curve that combines learning progress and prior spread to modulate the arbitration increment, whereas Eq. 5 uses an interval hard gate at the checkpoint level. Both follow the principle of using learning history to regulate prior influence. Figure 4 examines how quality gain continuously changes the arbitration increment in the smooth variant, while the additional performance comparisons for the final hard-gate method use the implementation in Eq. 5. We will explicitly clarify this distinction in the revision.

W2

1. The additional comparisons support higher mean performance from adaptive regulation on LeWM Reacher.

We retain the same Gaussian scoring formulation and use the same checkpoint, test starts, and planning budget within each comparison. Fixed λ is selected from six candidate values, using 40 validation evaluations per value, and then held fixed for testing.

The following results report mean ± SD across three independent prior-training seeds. The world model remains frozen, and each prior is evaluated on 75 test starts.

TaskPRISM success %Validation-tuned fixed λ success %BIPR success %
PushT76.44 ± 3.8580.00 ± 2.3180.89 ± 1.54
Reacher49.78 ± 6.1656.00 ± 8.1159.11 ± 2.04

This direct comparison distinguishes adaptive weighting from fixed regularization and provides additional evidence across independently trained priors.

2. Prior-degradation experiments further demonstrate the incremental value of adaptive regulation.

Under 25% and 50% action-label corruption on LeWM PushT, BIPR achieves mean gains of 2.67 and 5.33 percentage points over validation-tuned fixed λ, respectively. We also record learning progress, arbitration signals, applied weights, and search displacement to show how regulation enters candidate scoring. These results support its computational value under these prior-degradation conditions.

3. The additional evaluation overhead relative to the shared-prior baseline remains low.

BIPR reuses the same prior and world-model candidate evaluations, adding no trainable parameters or world-model rollouts. Under the original timing protocol, total evaluation wall-clock time increases by only 0.82% over PRISM, while evaluation time for the complete planner is 46.73% lower than CEM. These comparisons report incremental overhead and overall planning efficiency, respectively.

W3

Our evaluation focuses on planning with frozen world models in simulation, with real-robot evaluation as a future extension. We evaluate BIPR on two world-model backbones and four tasks covering contact-rich manipulation, precise reaching, and visual navigation, providing an experimental foundation for subsequent validation on real robots.

Q1

All experiments in this supplementary evaluation use the hard gate in Eq. 5. We have verified the training losses, learning progress, and gate state of each checkpoint, as reported below.

LinitL_{\mathrm{init}} and LbestL_{\mathrm{best}} denote the initial validation MSE and the lowest validation MSE over training, respectively, with q=clip((Linit−Lbest)/Linit,0,1)q=\mathrm{clip}((L_{\mathrm{init}}-L_{\mathrm{best}})/L_{\mathrm{init}},0,1). The gate is b(q)=1b(q)=1 when 0.15<q<0.300.15 < q < 0.30 and b(q)=0b(q)=0 otherwise.

BackboneTaskTraining seedPrior conditionLinitL_{\mathrm{init}}LbestL_{\mathrm{best}}qqb(q)b(q)
LeWMCube42Original1.0287230.6096500.4073720
LeWMPushT42Original0.9457130.7797790.1754591
LeWMReacher42Original1.0039680.9939900.0099390
LeWMTwoRoom42Original1.0075870.9335670.0734620
Sub-JEPACube42Original1.0259440.5405770.4730930
Sub-JEPAPushT42Original0.9465650.7842010.1715301
Sub-JEPAReacher42Original1.0038680.9937590.0100700
Sub-JEPATwoRoom42Original1.0060230.9327340.0728510
LeWMPushT0Independently trained0.9463010.7728260.1833191
LeWMPushT1Independently trained0.9465560.7663290.1904031
LeWMReacher0Independently trained1.0037870.9939040.0098460
LeWMReacher1Independently trained1.0041460.9939170.0101860
LeWMPushT4225% label corruption0.9457130.8668460.0833940
LeWMPushT4250% label corruption0.9457131.1379290.0000000
Sub-JEPAPushT4225% label corruption0.9465650.8697080.0811960
Sub-JEPAPushT4250% label corruption0.9465651.1262250.0000000

The gate state explicitly determines one of two reproducible regulation branches. When b(q)=1b(q)=1, Full uses prior anchoring with a fixed λ=0.5\lambda=0.5. When b(q)=0b(q)=0, Full uses prior anchoring with UCA, which provides online adaptation. The supplementary ablations match the prior checkpoint, evaluation starting states, planning budget, and random-seed protocol. Strictly equivalent branches share the same evaluation records.

Figure 4 analyzes continuous calibration behavior, while the final method is evaluated through controlled experiments using the hard gate in Eq. 5. In Figure 4, quality gain continuously modulates the arbitration increment using learning progress and prior spread. Eq. 5 selects the regulation branch at the checkpoint level. We will explicitly label Figure 4 as a supplementary analysis of the smooth calibration variant and provide a configuration-to-result mapping in the revision.

Q2

The supplementary results support an incremental benefit over validation-tuned fixed λ\lambda with independently trained priors on LeWM PushT and Reacher, and under prior degradation on LeWM PushT.

1. Validation-tuned fixed λ\lambda and independently trained priors

As reported in our response to W2, the fixed baseline selects λ\lambda from 0,0.25,0.5,0.75,1,2\\{0,0.25,0.5,0.75,1,2\\}, using 40 validation evaluations per candidate. Across three independently trained LeWM priors, BIPR achieves average success rates of 80.89±1.5480.89\pm1.54\\% on PushT and 59.11±2.0459.11\pm2.04\\% on Reacher, compared with 80.00±2.3180.00\pm2.31\\% and 56.00±8.1156.00\pm8.11\\% for the tuned fixed baseline. These values report the mean and standard deviation across three independently trained priors and support an average benefit across prior-training repetitions.

2. Incremental benefit under controlled prior degradation

On LeWM PushT, we corrupt the action labels in 25% and 50% of the training trajectories and independently retune the fixed λ\lambda for each condition. Each method uses the same 75 evaluation starting states. Results report the mean and standard deviation across three evaluation seeds.

Training-label corruptionValidation-tuned fixed λ\lambdaBIPR
25%70.67 ± 10.07%73.33 ± 12.22%
50%72.00 ± 14.42%77.33 ± 12.86%

BIPR improves average success by 2.67 and 5.33 percentage points, respectively, supporting its incremental value under these two prior-degradation conditions. The corresponding learning progress and gate states are reported in Q1.

3. Model error, conflict signals, and search displacement

On LeWM Reacher, we additionally scale the actions supplied to the world model while keeping the executed actions unchanged, measuring the response to controlled model mismatch.

World-model action-input scaleModel prediction MSEConflict signal vvNormalized search displacement from the prior
0.750.29530.03181.0024
0.500.67740.04251.0526

Model prediction MSE is measured on the same 75 offline windows. Conflict signals and search displacement are averaged over pre-success records from 75 online evaluation environments per condition. Stronger model mismatch is accompanied by a higher conflict signal, supporting its responsiveness to changes in model–prior disagreement under controlled errors. These diagnostics complement the success-rate comparisons by making the relationship among prediction error, regulation signals, and search behavior directly inspectable.

Q3

BIPR and GPC differ in how the prior enters planning, the optimization objective, and the search update. BIPR focuses on retaining prior influence in candidate scoring throughout search and adaptively regulating its strength.

ComparisonGPCBIPR
Role of the priorA diffusion policy generates action proposals or provides optimization starting pointsA Gaussian prior initializes search and explicitly regularizes candidate scoring in every round
Optimization objectiveSelects or optimizes actions according to world-model-predicted rewardsCombines goal cost and prior deviation through CWM+λjPC_{\mathrm{WM}}+\lambda_jP
Search and regulationGPC-RANK ranks candidates, while GPC-OPT performs action-gradient optimizationUses MPPI weighting to update the search mean and regulates prior strength using prior spread, model–prior disagreement, and checkpoint learning progress

We will cite GPC and the relevant literature in Related Work and explain these connections and differences to clarify BIPR’s specific contribution.

I thank the authors for the response. After looking at the response and the other reviewers' comments, I still feel the contribution of the work is incremental and therefore keep my original rating.

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Paper summary

Brain-Inspired Prior Regulation (BIPR) extends prior-guided MPPI by incorporating learned action priors throughout the planning process rather than using them only for initialization. The method introduces a persistent penalty for deviations from the learned Gaussian action prior and adaptively adjusts its strength based on prior uncertainty and disagreement between the world model and the prior. It further uses offline learning progress to calibrate this adjustment, without requiring additional trainable parameters or world model rollouts.

The authors evaluate BIPR on four simulated control tasks using two frozen world model backbones, LeWM and Sub-JEPA. Compared with PRISM, BIPR improves average success rates by 8.00 and 4.84 percentage points, respectively, with only 0.82% additional evaluation overhead.

Critical strengths

BIPR improves average success over PRISM from 75.00% to 83.00% on LeWM and 79.33% to 84.17% on Sub-JEPA under matched rollout budgets (Tables 1-2). These results support the practical value of incorporating prior information throughout planning rather than only during initialization.

BIPR requires no additional trainable parameters or world-model rollouts and introduces only 0.82% evaluation overhead relative to PRISM (Table 7). This makes the approach practical for existing world-model planning pipelines.

Critical weaknesses

The main performance gain comes from a Gaussian prior-relative penalty, which is closely related to standard prior regularization (Eq. 3). The proposed arbitration and calibration mechanisms rely on heuristic signals and thresholds, without sufficient justification for their connection to the neuroscience-inspired reliability principles motivating the method. Moreover, most of the improvement in the ablation study comes from fixed prior anchoring (Table 4), while a validation-tuned fixed regularization baseline is missing. This raises concerns about the novelty and necessity of the proposed adaptive mechanisms.

The experimental validation is limited relative to the paper's central claims. Component ablations are restricted to two tasks with one world-model backbone, and the experiments do not directly evaluate how adaptive regulation behaves under degraded prior quality, world-model prediction errors, or distribution shift. Such evaluations are important for understanding whether the proposed arbitration mechanisms are effective under the uncertainty and model–prior disagreement they are designed to address. Consequently, the experiments provide limited insight into when and why the adaptive mechanisms are beneficial.

Questions for authors
  • How does BIPR compare against a validation-tuned fixed prior regularization weight? Since prior anchoring accounts for most of the improvement (Table 4), this comparison is important for establishing the contribution of the proposed adaptive mechanisms.
  • What evidence supports using prior spread and model–prior disagreement as indicators for strengthening regularization? In particular, does the proposed arbitration remain effective when disagreement arises from an inaccurate prior rather than an unreliable world model?
  • How were the calibration thresholds in Eq. 5 determined, and how does the smooth quality gain evaluated in Appendix Figure 4 relate to the proposed hard-gate formulation? Clarifying which implementation was used in the reported experiments would help assess the contribution of metaplastic calibration.
3 comments

We thank the reviewer for recognizing the strengths of our work and address each comment point by point below.

W1

A large contribution from fixed anchoring does not imply that adaptive regulation adds no value. We additionally evaluated a validation-tuned fixed-λ baseline. Under the same planning budget, LeWM Reacher success increased from 56.00% ± 8.11% to 59.11% ± 2.04% across three independently trained prior heads. This supports an incremental benefit on this task.

Our contribution is to regulate prior influence using search evidence and learning history; the Gaussian penalty itself follows standard regularization. Arbitration responds to prior spread and model–prior disagreement, while calibration uses offline learning progress to determine whether to retain the adaptive increment.

The neuroscience connection is functional, motivating the combination of immediate evidence and slower learning history. The specific signals and thresholds are empirical design choices whose computational effects are evaluated through controlled comparisons. We will clarify this distinction and include the complete fixed-λ comparison in the revision.

W2

Following your suggestion, we conducted the following additional experiments.

1. Component ablations now cover two backbones and three tasks, supporting task-specific contributions of the adaptive mechanisms.

We added ablations of the prior-spread signal, conflict signal, and calibration mechanism. The table below presents comparisons with positive observed gains. Success rates are mean ± SD across three evaluation seeds, using a fixed prior checkpoint for each backbone–task pair and 50 evaluation starts per seed.

BackboneTaskAblationAblated success %Full success %Gain in pp
LeWMPushTWithout calibration, retaining PA+UCA82.00 ± 2.0083.33 ± 4.16+1.33
LeWMReacherWithout prior-spread signal58.67 ± 3.0662.67 ± 1.15+4.00
Sub-JEPAReacherWithout conflict signal53.33 ± 10.2655.33 ± 9.87+2.00
Sub-JEPATwoRoomWithout prior-spread signal89.33 ± 5.0392.67 ± 6.11+3.33

These comparisons support the contributions of prior spread, conflict, and calibration in the corresponding tasks, showing that the observed benefits extend beyond a single backbone.

2. Additional prior-degradation experiments show performance gains over fixed regularization.

We retrained the PushT priors with 25% and 50% action-label corruption and compared against validation-tuned fixed λ. The table lists corruption conditions with positive observed gains. Results are mean ± SD across three evaluation seeds, with 25 evaluation starts per seed.

BackboneCorruption levelTuned fixed λ success %Full success %Gain in pp
LeWM25%70.67 ± 10.0773.33 ± 12.22+2.67
LeWM50%72.00 ± 14.4277.33 ± 12.86+5.33
Sub-JEPA25%73.33 ± 12.8677.33 ± 16.17+4.00

These results show that the benefits are not limited to clean priors. Under the listed degradation conditions, adaptive regulation achieves higher mean success than validation-tuned fixed regularization, supporting its incremental value.

3. Our claim concerns the computational value of prior regulation under a limited planning budget.

We study how search evidence and offline learning history can regulate prior influence to improve planning with frozen world models and a fixed planning budget. World-model prediction-error calibration and general OOD robustness are outside our claimed contributions; regulation under distribution shift is already identified as future work in the conclusion. We therefore emphasize the value of prior regulation for planning, rather than a robustness guarantee against arbitrary model errors or distribution shifts.

Q1

As shown in our response to W1, BIPR achieves higher mean success on LeWM Reacher than the validation-tuned fixed-λ baseline, supporting the incremental value of adaptive regulation on this task.

Q2

A broader prior weakens the variance-normalized penalty, so increasing λ provides limited compensation. The disagreement term adds a bounded penalty when model-preferred candidates deviate further from the prior than the candidate batch as a whole. These signals regulate constraint strength; they do not determine whether the prior or the world model is more accurate.

Direct ablations support their contributions in the corresponding tasks. Removing the prior-spread signal reduces mean success by 4.00 percentage points on LeWM Reacher, while removing the disagreement signal reduces it by 2.00 percentage points on Sub-JEPA Reacher, as reported in W2.

Under the tested prior-corruption conditions, arbitration still achieves higher mean success than fixed anchoring. We keep the world model unchanged and compare PA with λ=0.5 against PA+UCA using the same corrupted prior. Full is equivalent to PA+UCA under these conditions, so this comparison directly tests the incremental contribution of arbitration.

BackboneLabel corruptionPA with λ=0.5 success %PA+UCA / Full success %
LeWM25%70.67 ± 14.0573.33 ± 12.22
LeWM50%70.67 ± 14.0577.33 ± 12.86
Sub-JEPA25%74.67 ± 16.1777.33 ± 16.17
Sub-JEPA50%62.67 ± 6.1165.33 ± 4.62

Results are mean ± SD across three evaluation seeds, with 25 evaluation starts per seed and a fixed prior checkpoint for each condition. This fixed λ=0.5 comparator differs from the validation-tuned fixed-λ baseline in W2.

These results support an incremental benefit of arbitration under the tested prior-degradation conditions, showing that the observed gains are not restricted to accurate priors.

Q3

The thresholds 0.15 and 0.30 were empirically determined through PushT planning experiments during development, frozen before the additional experiments, and kept fixed across both backbones. Based on checkpoint learning progress, the hard gate deterministically selects between base anchoring and full arbitration, making the calibration behavior directly interpretable and reproducible.

The quality gain in Figure 4 controls a continuous calibration curve that combines learning progress and prior spread to modulate the arbitration increment. Eq. 5 instead uses an interval hard gate based on checkpoint learning progress. Both implementations share the principle of using learning history to regulate prior influence. Figure 4 uses the smooth calibration variant to examine how quality gain continuously changes the arbitration increment, while the final method’s performance is evaluated through comparisons using the hard gate in Eq. 5. We will explicitly clarify this distinction in the revision.

Thank you for the rebuttal and additional experiments. The gate documentation and fixed-λ\lambda control are useful, but my central concern, that the adaptive mechanisms add value beyond a tuned fixed anchor, remains unresolved, so I will keep my rating.

  • BIPR’s margins over the tuned fixed λ\lambda (+3.11 on Reacher, +0.89 on PushT) lie within the baseline’s standard deviation, and the tuned fixed λ\lambda already recovers most of the gain over PRISM (49.78 to 56.00 on Reacher, 76.44 to 80.00 on PushT). The comparison covers only LeWM and two tasks.

  • Per the checkpoint table, q∈(0.15,0.30)q \in (0.15, 0.30) only for PushT, so calibration is a per-checkpoint switch between PA\mathrm{PA} with λ=0.5\lambda = 0.5 and PA+UCA\mathrm{PA}+\mathrm{UCA} rather than an adaptive mechanism. The thresholds were tuned on PushT, and under label corruption q≈0.08q \approx 0.08 or 00, so UCA is retained in every case and the gate is never shown to detect an unreliable prior.

  • In the model-mismatch diagnostics, vv moves only from 0.0318 to 0.0425, λ\lambda stays near 0.96, and no success rates are reported. The new ablation tables also list only conditions with positive gains, several smaller than the across-seed standard deviations.

Comments on the paper

1 comment

We thank the Area Chair and all three reviewers for their feedback. With the same action prior and planning budget, BIPR improves mean success across four tasks over PRISM by 2.00 percentage points on LeWM and 4.17 on Sub-JEPA in the supplementary hard-gate comparisons. Under the original timing protocol, BIPR adds only 0.82% evaluation time over PRISM, with no additional trainable parameters or world-model rollouts.

Reviewer UvPT

  • Does adaptive regulation improve on a tuned fixed weight? On LeWM Reacher, mean success rises from 56.00% to 59.11% across three independently trained priors. The matched Sub-JEPA Reacher comparison shows a 4.67-point gain. These are task-specific mean gains. We will report the full fixed-weight comparisons and ablations in the revision.
  • What does the gate do under prior degradation? The checkpoint gate retained UCA in all four label-corruption settings. With the same corrupted prior, adding UCA improved mean success over fixed anchoring by 2.67 to 6.67 points, isolating the contribution of arbitration under the tested degradation.
  • How does regulation respond to model mismatch? Under controlled mismatch on LeWM Reacher, the conflict signal increased from 0.0318 to 0.0425 while the regularization weight stayed near 0.96.

Reviewer EFbD

  • What is the contribution, and can the results be reproduced? BIPR keeps the prior active in candidate scoring throughout search and adjusts its weight using search signals. We reported gate states for 16 checkpoints and evaluated the hard-gate method under matched configurations. The revision will map results to their configurations and clarify the distinction from GPC. Our evaluation covers four simulated tasks.

Reviewer KaF1

  • How much do the components contribute? Persistent anchoring accounts for most of the gain. In matched hard-gate ablations, calibration improved mean success by 1.33 points on LeWM PushT, and retaining the conflict branch improved it by 2.00 points on Sub-JEPA Reacher. These effects are task-specific. The revision will distinguish the hard-gate ablations from Figure 4’s smooth calibration sweep.
  • Does the same weight configuration work across cost scales? When world-model cost and MPPI temperature were scaled together, BIPR achieved higher mean success than PRISM in all eight tested settings without retuning the regularization weight.

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