acceptodds
Under review as a conference paper at ICLR 2027

Planner-Aware Consequence Feedback for Coupling Task Assignment and Route Planning in Dynamic Multi-Agent Rescue

Abstract

Dynamic multi-agent rescue couples task assignment with route planning as haz-ards alter connectivity and traversal risk. We study how a learned dispatcher can use candidate routes returned by a fixed planner to inform target selection before commitment. We formulate Dynamic Multi-Rescuer Indoor Evacuation (DM-RIE), a centralized cooperative decision problem on dynamic multi-floor building graphs, and propose Planner-Aware Consequence Feedback (PACF), a modular planner-to-dispatcher interface. For each legal rescuer–target pair, a fixed plan-ner supplies currently feasible route candidates; PACF encodes their context and aggregates learned candidate scores into a target-logit correction. Mission-level rewards jointly train the dispatcher and PACF, while candidate generation, fea-sibility checking, and route selection follow fixed planner rules. Under a com-mon execution protocol and building-disjoint splits, evaluations over three train-ing seeds show that adding PACF increases mean Test rescue rates from 91.90% to 92.71% for the MAPDP-based dispatcher and from 90.51% to 93.48% for the MAPT-based dispatcher. Improvements vary across training seeds and task con-ditions. These results support the usefulness of planner-derived route context for learned target selection in the DMRIE benchmark.

Primary area:
reinforcement learning
Keywords:
multi-agent reinforcement learning, task assignment, route planning, planner-policy feedback, dynamic multi-agent rescue

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_mhgcOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper proposes a Planner-Aware Consequence Feedback method, which allows a multi-agent dispatcher in dynamic indoor rescue scenarios to incorporate the set of candidate routes returned by the planner into target selection before making the final decision. Meanwhile, the paper also introduces a new benchmark for the corresponding scenario. Theoretical analysis and experimental results are provided to validate the performance advantages of the proposed method.

Critical strengths
  1. The motivation of this paper is clear. The method first obtains candidate-route information for different targets, compares the targets using the route information, and then makes the final target decision. This addresses a practical and intuitive limitation of conventional methods.
  2. This work also constructs a benchmark and dataset for the corresponding scenario, which effectively and accurately match the problem setting studied in the paper and enable evaluation in this specific scenario.
  3. The modular design of the proposed method allows it to be flexibly integrated with other methods.
Critical weaknesses
  1. The authors make several assumptions that may not be sufficiently realistic, such as assuming the exact locations of the targets and access to the global hazard state. These assumptions limit the applicability of the proposed method to some extent.
  2. From the experimental results, the performance improvement brought by the proposed method is relatively limited. In some cases, especially at the Medium level, there is even a considerable performance gap compared with conventional methods.
  3. In the comparison experiments, the authors mainly compare against conventional methods and the two base methods, MAPDP and MAPT. Comparisons with other dynamic multi-agent rescue methods are missing, which makes it difficult for reviewers to accurately assess the effectiveness of the proposed method. Minor Comments
  4. The proposed method seems to depend on several specific hyperparameters, such as the number of candidate routes and the setting in the Per-route Scoring block where zijkz_{ijk} is mapped to a bounded score with qmax⁡=4q_{\max}=4. If these values are fixed and not tunable, the authors should provide corresponding explanations. Otherwise, the authors should explain why these values are chosen and provide parameter sensitivity experiments.
  5. The current manuscript lacks a complete and detailed ablation study. PACF is not an indivisible module. Therefore, adding an ablation study section to analyze the role of different components in more detail would help readers better understand the effectiveness of each component in the proposed method.
  6. The main motivation of PACF is to utilize several candidate routes. Intuitively, different numbers of candidate routes should lead to different performance gains. Therefore, the authors should report and analyze the performance and computational cost under different numbers of candidate routes.
Questions for authors
  1. In Table 1, adding PACF to MAPDP leads to a performance decrease at the Medium level, while the improvement at the Hard level is also very limited. Moreover, at the Medium level, there is still a performance gap compared with conventional methods such as Nearest and Hu. I appreciate that the authors report and discuss the experimental results honestly and accurately, but the current results are still somewhat confusing. Could the authors explain this phenomenon? Is it related to the benchmark setting?
  2. The authors assume that the exact locations of the targets are known. Have the authors considered a more realistic setting where only approximate target locations are known, or where the targets can move within a small region around their known locations? If PACF remains effective under such a more realistic setting, it would help improve the applicability of the proposed method.
3 comments
AuthorsOpenReview ↗

Performance, conventional and external baselines

Thank you for recognizing the motivation and modular design. We address all three weaknesses, three minor comments, and two questions in three comments: performance/baselines, sensitivity/ablations, and assumptions/robustness. W, M, and Q follow their order in your review.

W2: Gains and conventional methods

We expanded evaluation to 60 buildings disjoint from Train/Validation, 20 per difficulty, with ten initializations each (600 scenarios). Rescue counts completed evacuation, averaged within buildings and difficulty, then weighted 12:18:24. All methods share risk-weighted candidate planning, minimum-cost route execution, legal masks, commitments, and service rules. Neural methods use five training seeds, stochastic allocators five search seeds, and deterministic rules one rollout per scene.

MethodMedium (%)Hard (%)Expert (%)Weighted (%)
MAPDP Base99.7896.7689.0394.00
MAPDP + PACF99.8698.5093.0796.39
MAPT Base99.8096.6890.7394.73
MAPT + PACF99.9799.0393.3596.71
RMCA-adapted100.0098.0692.5996.06
Nearest99.8396.8388.1093.62
Hungarian99.8396.3988.4293.61
Risk Hungarian99.8396.9287.3893.32
SA, budget 6099.3487.8763.7379.69
GA, budget 6099.6592.5280.0388.55

Five-seed sample SDs for MAPDP Base/PACF are 1.47/0.58 pp; for MAPT 0.85/0.50 pp. Paired gains are positive in all five seeds per backbone. Mean gains are +2.39 pp (MAPDP, 95% building CI [1.96, 2.85]) and +1.98 pp (MAPT, [1.52, 2.46]). CIs condition on fitted ensembles, not future retraining; differences use unrounded values.

We also completed all SA/GA budgets rather than selecting one:

Objective evaluations per solveSA mean (%)GA mean (%)
6079.6988.55
18077.2583.12
60078.6978.89

All 18,000 episodes, including truncations, remain included. The cost oracle matches execution, but the coverage-first nominal chain-cost surrogate does not predict future hazards or victim health. More search does not monotonically improve terminal rescue. Equal objective counts do not imply equal wall-clock budgets.

Q1: The original Medium decline and small Hard gain

We retain the original three-seed counterexample: MAPDP + PACF scored 95.66% at Medium versus 100% for Nearest/Hungarian. Extending the original Test to five seeds still gives MAPDP a -1.15 pp Medium difference, so a single unfavorable seed does not explain it.

DifficultyOriginal five-seed gain: MAPDP/MAPT (pp)Current gain: MAPDP/MAPT (pp)
Medium-1.15 / +3.02+0.08 / +0.17
Hard+3.33 / +3.06+1.74 / +2.35
Expert+2.34 / +2.55+4.03 / +2.61

Current Medium results are near saturation, limiting absolute gains. This does not explain why the original PACF model was worse. Few original buildings, training across mixed difficulties, and seed variation are plausible contributors, not verified causes. Both layouts and initializations changed, so the sign change cannot be assigned to either alone. Hard gains also vary by backbone and protocol. We claim scenario-dependent improvements over matched Base models, not uniform superiority.

W3: External assignment-and-planning comparator

We added RMCA-adapted from Chen et al., Integrated Task Assignment and Path Planning for Capacitated Multi-Agent Pickup and Delivery. We checked the author implementation, then implemented a separate rescue adaptation: regret-based request insertion and six LNS rounds, destroying 25% of requests per round. Requests are waiting room-level victim batches; insertion costs use the common planner and current service/queue estimates. The method respects commitments and shares rescue/carrying/handoff execution, without hidden health or future hazards.

DMRIE imposes no additional hard carrying capacity and does not reproduce the original collision-avoidance guarantees. This is an adapted external allocator, not an unchanged reproduction or native fire-rescue algorithm.

On 3,000 episodes, RMCA obtains 96.06 ± 0.25% (five search seeds). PACF-minus-RMCA is +0.33 pp for MAPDP (building CI [-0.48, 1.19]) and +0.65 pp for MAPT ([-0.23, 1.57]). Both include zero; no advantage over RMCA is established. Search and training seeds are not paired.

CPU median/p95 decision latency is 19.00/356.05 ms for RMCA versus 33.69/112.51 for SA-600 and 32.48/112.93 for GA-600, measured serially on fixed Train contexts (240 samples/method). Host-wide exclusivity was not established; this is not equal-time rescue quality or a GPU throughput ranking. Other stochastic-hazard rescue frameworks were reviewed but not all implemented, so external-method coverage remains partial.

AuthorsOpenReview ↗

Retrained sensitivity and component controls

M1/M3: Candidate counts, score bounds, and computational cost

These are tunable design choices. Executable cap kk limits retained route candidates; KK limits routes visible to feedback; qmax⁡q_{\max} bounds learned scores. Defaults are k=K=3k=K=3, qmax⁡=4q_{\max}=4, and raw candidate budget six. They bound representation size and correction magnitude; they are not claimed optimal.

We completed separate full MAPT retraining runs for all six variants below, each with seed 1, 64 epochs/8,192 episodes and Validation-only selection. The default is the matching seed-1 checkpoint, not the five-seed mean. All are evaluated on the same 600 scenarios (60 buildings × ten initializations), with difficulty weights 12:18:24.

kKq_maxRescue (%)Difference (pp)95% building CI
33496.060.00Reference
31496.49+0.43[0.03, 0.82]
32496.91+0.84[0.24, 1.48]
33296.47+0.41[0.04, 0.77]
33896.69+0.62[0.06, 1.23]
11497.13+1.06[0.44, 1.74]
22495.69-0.37[-0.91, 0.11]

Differences are computed before rounding. These are retraining comparisons, not inference-time substitutions. The CIs use 10,000 paired building resamples in six difficulty-by-generator strata, retain all initializations, and condition on a single fitted seed per setting. They do not establish rankings across future training seeds and are unadjusted for multiple comparisons. Truncated outcomes remain included.

Neither more candidates nor larger bounds yield monotonic gains. The k=1k=1 model has the highest observed mean, so several retained routes are not necessary for the best result here. With one candidate, PACF still feeds route information into target choice. We retain the original default instead of reselecting it on Test. The candidate cap is an upper bound: fewer routes may be feasible.

Actual cap k (all retained routes visible)L40 median / p95 (ms)
125.51 / 30.74
225.55 / 31.61
325.76 / 32.06

Separately, at fixed k=3, median/p95 values are K=1: 26.00/32.40; K=2: 26.27/32.64; q_max=2: 25.45/31.86; q_max=8: 25.54/32.12 ms, versus 25.37/31.76 for the matched default. These small differences do not establish a speed ranking. Timing includes candidate construction and neural decisions, using 24 Train-context labels (20 states), three warmups and ten repeats, synchronized L40 inference and normal caches. Loading and environment advancement are excluded; host-wide exclusivity was not established. Raw construction/first-hop searches persist at smaller caps, so retained-count reductions do not yield proportional savings.

M2: Input ablations and information/capacity controls

These two groups answer different questions. All use common MAPT training seeds 1–3, the same budget, Validation selection, and 600 scenarios. ± denotes sample SD across training-seed aggregate rates. Conditional building CIs describe fitted ensembles, not future retraining.

Input conditionRescue (%)Difference from Full (pp)95% CI
Full PACF96.64 ± 0.660.00Reference
Relative statistics, no route tokens95.27 ± 1.38-1.36[-1.97, -0.81]
First-hop + statistics96.55 ± 0.40-0.09[-0.40, 0.20]
No observed hazard trends96.16 ± 1.09-0.48[-0.69, -0.27]

Removing tokens or trends lowers the mean. The first-hop CI includes zero, so complete routes are neither established as necessary nor proved equivalent to first-hop information.

Integration/capacity controlRescue (%)Control − PACF (pp)95% CI
Base94.86 ± 1.08-1.77[-2.42, -1.11]
Route-free capacity control93.63 ± 2.41-3.01[-3.47, -2.55]
Ordinary route head97.02 ± 0.34+0.39[0.10, 0.69]
Fixed minimum-cost bias96.74 ± 0.22+0.10[-0.17, 0.39]

Active parameters are PACF 594,170, Ordinary 594,298, capacity control 594,493, versus Base 223,677. The capacity control uses Base inputs only; parameter matching does not equate function classes. Ordinary mean-pools the same route representations before standard target scoring, with independently trained encoders and random initialization; PACF scores before aggregation and initializes feedback at zero. Fixed feedback retrains with a Train-normalized minimum-cost bias, coefficient one, without a learned scorer.

These results support planner-derived information across several designs. They do not establish a unique benefit of PACF aggregation: Ordinary is higher, and fixed feedback is competitive. This is a component study, not a full factorial analysis.

AuthorsOpenReview ↗

Environment assumptions and location robustness

Comment

W1: Scope of the environment assumptions

We agree that exact target locations and centrally available hazard observations limit operational applicability. DMRIE is a controlled simulation platform for dispatch after a coordinator receives observations, not a validated deployment system. It does not model how reliable sensing or communication is achieved. Victim health is hidden from both actor and critic, and finite hazard trends need not form a sufficient belief state. The formulation is centralized partially observable control with variable-duration decision epochs, not a fully observed MDP or decentralized learning.

Known maps/targets also occur in assignment-and-planning studies, but that precedent does not prove realism. We therefore tested two specific relaxations of the location assumption, while retaining reliable communication and current hazard observations.

Q2: Approximate locations and local target movement

Frozen policies were evaluated on the first initialization of each of the 60 buildings, six policy families, three training seeds, and five conditions: 5,400 episodes. This is a 60-scene subset, not all 600 main scenarios. The 1,080 unperturbed episodes exactly reproduce their archived outcomes. Rescue rates use the same within-building/difficulty aggregation and difficulty weights 12:18:24; ± is training-seed sample SD.

For location errors, every 30 s a waiting victim is reported in a neighboring same-floor room within 10 m with probability 0.10 or 0.30. Physical positions do not change. Positive inspection confirms the room; negative inspection clears the false report until the next refresh without revealing the true room. Observations, masks, and commitments use these reports consistently. Victim identity/lifecycle remain centrally available, so this is not unrestricted search for unknown victims.

For movement, eligible waiting victims attempt a move every 60 or 30 s within the initial room and its one-hop same-floor neighborhood, within 10 m. Moves require passable spaces, exclude stairs/safe areas, and cannot occur during service, carrying, or rescuer co-location. Current positions remain exactly observed. Thus movement and uncertain reports are separate interventions, not combined uncertainty and motion.

Perturbation draws are keyed by scene, victim, and time independently of hazard randomness. All methods share the exogenous rule, though actions can change realized movement eligibility. All outcomes are retained.

ConditionMAPDP BaseMAPDP PACFMAPT BaseMAPT PACFMAPT OrdinaryMAPT Fixed
Unperturbed95.22 ± 1.0497.53 ± 1.0895.93 ± 0.7997.41 ± 0.8198.06 ± 0.5697.07 ± 0.75
Location error 10%95.49 ± 0.5497.50 ± 0.3395.62 ± 0.8997.59 ± 0.8197.81 ± 1.0297.07 ± 0.14
Location error 30%95.52 ± 0.4396.20 ± 1.2892.25 ± 1.1996.76 ± 0.0996.36 ± 0.7895.83 ± 0.32
Motion every 60 s95.00 ± 0.9196.82 ± 1.2394.26 ± 1.4597.35 ± 0.7798.24 ± 0.3397.50 ± 0.73
Motion every 30 s95.19 ± 0.5696.91 ± 1.6593.02 ± 1.1797.07 ± 0.7597.59 ± 1.2097.01 ± 0.05

All rates are percentages. Paired differences use unrounded results:

PerturbationMAPDP gain (pp)95% building CIMAPT gain (pp)95% building CI
Location error 10%+2.01[0.52, 3.64]+1.98[0.74, 3.18]
Location error 30%+0.68[-0.52, 1.91]+4.51[2.69, 6.39]
Motion every 60 s+1.82[0.71, 3.02]+3.09[1.57, 4.57]
Motion every 30 s+1.73[0.34, 3.27]+4.04[2.04, 6.08]

MAPT gains remain positive with conditional CIs above zero in all four perturbations. At 30% location error, its Base rate falls from 95.93% to 92.25%, while PACF falls from 97.41% to 96.76%. The larger gap reflects less degradation, not improvement caused by errors. MAPDP also has positive mean gains, but its 0.68 pp location-error gain has a CI containing zero. Ordinary remains competitive and often higher, so robustness is not unique to PACF aggregation.

The CIs condition on the fitted three-seed ensembles and sampled first initializations. These tests address the specified local disturbances, not uncertain global hazards, communication failures, unknown victim identities, unrestricted human movement, or real-world deployment. The revised claims retain those boundaries.

Reviewer_8TmDOpenReview ↗
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2
Confidence
2
Informativeness
2
Presentation
2
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2
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Paper summary

This paper studies the task assignment and route planning in dynamic indoor rescue. It proposes the DMRIE benchmark and Planner-Aware Consequence Feedback(PACF), an interface that encodes candidate routes from a fixed planner and aggregates learned route scores into corrections to the dispatcher's target-selection logits. The dispatcher and feedback module are jointly trained using mission-level rewards, while route generation and selection follow fixed rules. On building-disjoint test tasks, PACF improves mean rescue rates for MAPDP- and MAPT-based dispatchers.

Critical strengths
  1. DMRIE enables investigation into a practical question: whether a currently reachable target is worth committing to.
  2. The interface between the planner and the learned strategy is well-defined, with largely self-consistent implementation logic. PACF preserves fixed feasibility checks and route execution rules, incorporates task-reward supervision through differentiable goal refinement, and supports integration with parallel MAPDP as well as autoregressive MAPT.
Critical weaknesses
  1. The paper could provide clearer discussion on how its experimental setup specifically examines the coupling between task assignment and routing. Characterizing the availability of alternative routes and hazard-induced changes in connectivity would help further validate the diagnostic value of this scheme as a benchmark.
  2. The comparison between the baseline model and PACF does not clearly disentangle the contribution of route context from that of the proposed scoring and aggregation mechanism. An important baseline is missing: under comparable model capacity and training budgets, the same route embeddings are directly fed into the target-selection decoder via concatenation with a standard scoring head.
Questions for authors
  1. Could the authors further clarify the contributions of DRMIRE when used as a benchmark?
  2. What advantages does the proposed method have relative to simpler route-conditioned dispatch strategies?
3 comments
AuthorsOpenReview ↗

Platform contribution and coupling evidence

Thank you for recognizing the motivation and modular interface. We address both weaknesses and both questions in two comments, covering the platform here and ordinary fusion next. W and Q follow their order in your review.

Q1: What DMRIE contributes

We distinguish the graph-based simulation platform, its finite evaluation suite, and PACF as one interface tested within it. Changing fire, smoke, and passability affect routes during target commitments. Arrival is followed by rescue service, carrying, handoff, and safe-area evacuation queues. Thus current reachability or arrival alone does not determine successful evacuation. The platform supports controlled comparisons of route-informed target selection under these execution rules.

Assignment–path coupling itself is not new. The distinctions concern information, dynamics, and completion semantics:

SettingPath information for allocationDynamics and completion
MAPDPDistances and vehicle/task relationsGiven paired tasks; capacity/precedence and same-vehicle pickup/delivery; distance objective
MAPTStation travel times and relationsOnline requests; current requests observed centrally, future ones unknown; capacity/profit and commitments
Chen et al., capacitated MAPDConflict-aware space-time path costsKnown static map; offline/online requests; capacity, precedence, and collision constraints
Tihanyi et al.Safety probabilities and marginal allocation valuesKnown map/targets/hazard model; stochastic spread; visit targets and exit safely
DMRIE with PACFCurrent hazard-aware candidate routes before commitmentCentrally shared current observations; evolving passability; rescue, carrying, handoff, and evacuation queues

DMRIE contributes this reproducible combination of rescue dynamics and execution semantics, not the first use of paths in assignment or a physically validated emergency system. It provides no space-time MAPF collision guarantee. Reliable communication and current graph observations are assumptions; hidden victim health makes the controller partially observable. Its diagnostic value does not require PACF to beat every fusion rule.

The evaluation contains 60 buildings disjoint from Train/Validation, 20 per difficulty, each with ten randomized initializations. Six floors and three rescuers are fixed:

ConfigurationMediumHardExpert
Graph nodes: mean (range)96210.9 (207–215)322.9 (316–331)
Victims / occupied rooms12 / 618 / 924 / 12
Initial fires145
Safe spaces / stair shafts2 / 12 / 21 / 3

Nodes are room/corridor/stair spaces, excluding navigation connectors. Initializations vary fire/victim/rescuer placements, not building difficulty. These are 60 layouts from one compositional generator, not 600 independent buildings. The two generator labels differ in branch depth only at Expert. The layouts were already evaluated under an earlier initialization protocol, so the extension is not a second untouched holdout. We claim controlled instance coverage, not unrestricted architectural generalization.

W1: Does assignment–routing interaction actually occur?

We selected the first two buildings per difficulty-by-generator stratum and their first initialization before inspecting diagnostic outcomes. Two seed-1 PACF models on 12 scenes give 24 trajectories, 4,472 joint decisions, and 7,778 policy ticks. Action-neutral logging exactly preserves archived actions and outcomes.

DiagnosticMAPDPMAPT
Valid pair observations2,4452,510
Pairs with 2–3 candidates929 (38.00%)957 (38.13%)
Conditional top-target changes120/434 (27.65%)157/454 (34.58%)

Target changes remove only feedback while fixing weights, states, masks, and actual decoding prefixes. All 5,439 selected routes remain minimum-fixed-cost choices. These repeated visited-state measurements demonstrate route alternatives and target influence, but are not a closed-loop removal experiment or independent samples from all 600 scenes.

Nineteen trajectories develop newly blocked nodes. Holding preceding origins and waiting-target sets fixed while changing only passability produces 20 reachability losses across four trajectories, with passable endpoints; six safe-target losses also occur. The other 20 trajectories have no waiting-target reachability loss. All outcomes, including ten incapacitations, remain included. These diagnostics verify active connectivity changes without causally assigning shares of the rescue gain to each mechanism.

AuthorsOpenReview ↗

Ordinary fusion, capacity controls, and claims

W2: Same route inputs and an ordinary target-scoring head

We implemented the requested comparison. Ordinary fusion uses the same route inputs and encoder architecture as PACF, with independently trained weights. It masked-mean-pools valid 644-dimensional candidate representations, concatenates the backbone pointer score, and predicts target logits through a 645→128→64→1 MLP. PACF scores routes before normalized soft-min aggregation and adds an explicit bounded correction. Ordinary uses random initialization; PACF initializes feedback at zero. This compares complete integration designs, including initialization, rather than isolating soft-min alone.

All controls use MAPT, common training seeds 1–3, the same 64-epoch/8,192-episode budget and planner, Validation-only selection, and 600 scenarios (60 buildings × ten initializations). Rescue measures completed evacuation, averaged within building and difficulty with weights 12:18:24. ± is training-seed sample SD; differences use unrounded values. The 95% building-bootstrap CIs condition on fitted models, do not estimate future retraining variability, and are unadjusted for multiple comparisons.

ModelRescue (%)Model − PACF (pp)95% CI (pp)
PACF96.64 ± 0.660.00Reference
Base94.86 ± 1.08-1.77[-2.42, -1.11]
Route-free capacity control93.63 ± 2.41-3.01[-3.47, -2.55]
Ordinary route head97.02 ± 0.34+0.39[0.10, 0.69]
Fixed minimum-cost bias96.74 ± 0.22+0.10[-0.17, 0.39]

Ordinary exceeds PACF by 0.39 pp; fixed feedback has a higher mean with a CI containing zero, which does not establish equivalence. These results do not support superiority of PACF aggregation over simpler route-conditioned strategies.

ModelActive actor/critic parameters
Base223,677
PACF594,170
Ordinary594,298
Route-free capacity control594,493

Shared parameters are counted once and disabled branches excluded. The capacity control adds a residual scorer using only Base decoder state, target embedding, and pointer score, without routes or extra history. PACF exceeds it by 3.01 pp (CI [2.55, 3.47]), weakening a parameter-count-only explanation. This exploratory control does not equalize function classes or optimization difficulty.

Fixed feedback subtracts the minimum candidate cost, normalized by Train-only mean 4.16884 and SD 2.14576, from target logits with coefficient one. The dispatcher is fully retrained without a learned route scorer; scaling is not selected on Test. Separately, removing route tokens while retaining relative statistics gives 95.27 ± 1.38%, 1.36 pp below PACF (CI [0.81, 1.97]). These controls support using planner information, not a unique benefit of per-route scoring.

Q2: What advantages are actually supported?

The five-seed comparison supports improvement over the matched Base models on the same 600 scenarios:

BackboneBase (%)PACF (%)Gain (pp)95% building CI
MAPDP94.00 ± 1.4796.39 ± 0.58+2.39[1.96, 2.85]
MAPT94.73 ± 0.8596.71 ± 0.50+1.98[1.52, 2.46]

All five paired gains are positive for each backbone. These are modest absolute improvements, not evidence that PACF is the best fusion rule. The three-seed controls above must not be compared as if they were five-seed ensembles.

We retain PACF as the explicit interface investigated: bounded route scores, a separate correction to backbone preferences, and zero initial feedback. With equal candidate scores the normalized aggregate is independent of count; this is not invariance to arbitrary duplication. These properties have not been shown to improve optimization, generalization, or safety over Ordinary.

Decision timing on L40Median (ms)p95 (ms)
MAPT Base26.3132.80
PACF25.4531.81
Ordinary25.4131.81
Fixed cost21.3027.72

Timing includes candidate construction and neural decision processing on 24 Train-context labels (20 distinct states), three warmups and ten measured repeats per context. Inference is synchronized; normal caches are retained and state/history reset. Loading, warmup, and environment advancement are excluded; host-wide exclusivity was not established. The small PACF/Ordinary difference is not a latency advantage. The supported conclusion is that planner-derived information helps target selection through several designs, with Ordinary stronger in this comparison.

I sincerely thank the authors for this thorough and transparent rebuttal—the newly added controls are exactly what I hoped to see. That said, the ordinary-fusion comparison shows a simpler route head slightly outperforming PACF, which makes it difficult for the proposed mechanism's specific contribution to stand. The DMRIE benchmark itself seems valuable, but I remain unsure what central problem the paper, as currently framed around PACF, answers.

I therefore keep my score unchanged.

Reviewer_kbcDOpenReview ↗
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2
Confidence
3
Informativeness
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1
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Paper summary

The paper studies multi-rescuer evacuation in buildings where fire and smoke change which paths are usable over time. It proposes PACF, a module that takes the candidate routes produced by a fixed planner for each rescuer–target pair, scores them, and uses the aggregated score to adjust the dispatcher's target probabilities before a target is chosen. The module is trained jointly with the dispatcher using PPO and is added to two existing dispatchers, MAPDP and MAPT.

Critical strengths
  1. The problem is well motivated. In a building fire, which target a rescuer should go to depends on whether good routes to the target remain available, and the paper makes a reasonable case for bringing this route information into the target choice rather than only using it after the target is fixed.

  2. PACF is modular and does not depend on a specific dispatcher. The authors add it to two quite different backbones (parallel and autoregressive) and compare each against a matched baseline that shares the same planner, training budget, and checkpoint selection.

  3. The evaluation uses building-disjoint Train/Validation/Test splits, and the results are reported honestly. The paper shows per-seed results, breakdowns by difficulty and hazard placement, and cases where PACF does worse, and it also measures the added decision latency.

  4. The new DMRIE benchmark and the detailed appendix (architecture, training configuration, evaluation seeds) should make the work reasonably easy to reproduce, especially if the code and checkpoints are released.

Critical weaknesses
  1. (Major) The experimental evidence is not fully convincing. For MAPDP, the gain from PACF is 0.81 pp, which comes from +7, +14, and 0 extra rescues out of 864 across the three seeds. For MAPT, the gain is 2.97 pp but with an SD of 2.48, and seed 1 is actually worse than the baseline. The Test set is also smaller than it looks. It has 48 tasks, but they come from only 12 buildings, and the four tasks of each building share the same layout, victims, and rescuer starts. App. B.2 also says that some recipe labels share the same initial configuration, so some tasks are duplicates. This also makes the per-hazard breakdown in Table 3 hard to interpret. I would ask the authors to use at least 5 seeds and to report confidence intervals or a paired significance test.

  2. (Major) App. D.1 says that "Test outcomes were inspected during development." This is a serious concern. The paper puts a lot of weight on building-disjoint splits and Validation-based checkpoint selection, but if Test results were looked at during development, they may have influenced design or hyperparameter choices. The authors should explain what this inspection involved and whether any decisions were made based on it.

  3. (Major) The comparison with the heuristic baselines may not be fair. Section 4 says all methods share the same execution protocol. However, App. D.1 says the heuristics follow shortest-nominal-duration routes, while the learned methods use the risk-weighted planner (β = 2, Eq. 29). That difference alone could favor the learned methods. The heuristics are also run with a single seed, and SA and GA get only 60 evaluations per decision, which is a small budget. Even under these conditions, Nearest and Hu reach 100% on Medium tasks while both PACF models get 95.66%. The learned Base models are also barely better than Hu overall (91.90% and 90.51% vs. 90.39%). I would like to see the heuristics run with the same planner as the learned methods before drawing conclusions from this comparison.

  4. (Major) The novelty is limited. In practice, PACF is a learned bias added to the target logits, computed from route features. The theory in Appendix A is mostly standard results: the soft-min is the minimum of a KL-regularized objective, and the corrected softmax is the solution of a KL-regularized problem. Prop. A.3 is the only result that relates the method to return, but it depends on a calibration error ε that the authors say they do not measure. So it does not tell us much about the trained model. The paper also states that the candidate scores are latent features and "not explicit route-return estimates." This does not fit well with the title, since "Consequence Feedback" suggests the module estimates the consequences of choosing a target.

  5. (Major) There is no analysis of what PACF actually learns. The paper does not check whether C_ij correlates with planner cost, hazard risk, or the number of alternative routes. It also gives no example of a case where route information changes which target is selected. Without this, it is hard to know whether the gains come from the route information or simply from the extra parameters and inputs, since the Base model sets C_ij = 0 and does not see the route features at all. The two backbones also behave in opposite ways on stair-pressure tasks (+63 rescues for MAPT, −9 for MAPDP), and the paper does not try to explain this.

  6. (Minor) The notation is overloaded in several places, which makes the paper harder to follow. In Eq. 1 (line 87), r is an executable path, but a few lines later (line 97) r_n is the team reward and r(·) is the reward function. I would keep r for the reward and use another letter for routes. There are other cases too. τ is used for the event time τ_t and for three different temperatures (τ_A, τ_R, τ_P). d is used for the elapsed steps d_t, the edge duration d_e, and the network width. P is the transition function, the victim set, and later the number of rescuer–target pairs. A pass over the notation would help.

  7. (Minor) The paper says the problem is modeled as an MDP, but on line 107 the policy acts on an observation o_t = Ω(s_t), not on the state. An observation function by itself would be fine if Ω kept all the state information, but here it does not. Victim health is not among the observed features (App. C.1.1), even though incapacitation and the evacuation reward depend on it. PACF also uses the previous observation to compute hazard trends, which suggests the current observation is not Markov on its own. So the problem is partially observable. Decisions are also made at events of variable length with γ^{d_t} discounting, which is closer to a semi-MDP. The formulation should describe the problem as it actually is.

  8. (Minor) It is not clear to me why the problem and the method are framed as multi-agent when both training and execution are centralized. A single coordinator sees the full observation and chooses the actions of all rescuers. This is a single-agent problem where the action is the joint action of the team, and the factorization in Eq. 3 is just one way to parameterize that joint action. I understand that "multi-agent" may refer to the multiple rescuers in the environment rather than to the learning setup. If so, the paper should say this explicitly and avoid the MARL-style terms like "agent-level policy." It would also help to discuss whether centralized execution with full observation is realistic in a building fire, where communication is likely to be unreliable.

Questions for authors
  1. Can you report results with more seeds (at least 5), along with confidence intervals or a paired significance test? MAPDP gains no rescues on one seed and MAPT loses rescues on another, so I am not sure the overall improvement is reliable.

  2. App. D.1 says Test outcomes were inspected during development. What exactly was inspected, and at what stage? Did any design, hyperparameter, or checkpoint-selection decision depend on Test results?

  3. Why do the heuristic baselines use shortest-nominal-duration routes instead of the risk-weighted planner used by the learned methods? How do they perform when they use the same planner?

  4. The Base model sets C_ij = 0 and never sees the route features. How do you separate the effect of route information from the effect of extra parameters and inputs? For example, how does PACF compare with a fixed bias such as C_ij = min_k b_ijk, or with a variant that feeds the route features to the backbone without the logit correction?

  5. What does C_ij actually learn? Does it correlate with planner cost, hazard risk, or the number of alternative routes? A concrete example where the route information changes the selected target would help support the "consequence feedback" interpretation.

4 comments
AuthorsOpenReview ↗

Reliability and Test-use history

Comment

Thank you for the careful assessment and for recognizing the motivation and modular interface. We address all five major concerns, three minor comments, and five questions in three comments, grouping overlapping points. W, M, and Q follow their order in your review.

W1/Q1: Five seeds, repeated states, and uncertainty

We agree that the original 48 task labels were not independent layouts: they came from 12 buildings and contained 43 distinct initial states. Hazard-placement rules shared victim/rescuer placements and sometimes produced duplicate initial states.

The expanded evaluation uses 60 buildings disjoint from Train/Validation, 20 per difficulty, with ten initializations per building (600 scenarios). Each initialization randomizes fire locations, victims, and rescuer starts while fixing the building and difficulty. All generated outcomes are retained. We average within buildings and difficulty, then apply fixed difficulty weights 12:18:24. Each model receives 64 epochs/8,192 training episodes and Validation-only checkpoint selection.

BackboneBase (%)PACF (%)Gain (pp)95% building CI (pp)
MAPDP94.00 ± 1.4796.39 ± 0.58+2.39[1.96, 2.85]
MAPT94.73 ± 0.8596.71 ± 0.50+1.98[1.52, 2.46]

Here ± is sample SD over five training seeds; pp means percentage points. Paired gains for seeds 1–5 are MAPDP: 2.08, 1.02, 1.31, 3.77, 3.78 pp; MAPT: 2.28, 1.40, 1.65, 1.63, 2.95 pp. All ten gains are positive. Differences use unrounded values.

The CIs use 10,000 paired building-bootstrap draws within six difficulty-by-generator-label strata, retaining all ten initializations per building. They condition on fitted models and do not estimate future retraining variability. There are 60 layouts, not 600 independent layouts. The generator labels differ in branch-depth rules only at Expert; this is broader coverage within one generator family, not broad architectural transfer.

Ten initializations were fixed before their outcomes, as a budget choice rather than a power calculation. Over 1,000 paired subset resamples, the 95th-percentile absolute deviation from the ten-draw gain falls from 0.789 to 0.406 pp for MAPDP, and 0.639 to 0.315 pp for MAPT, when using two versus five initializations. This supports repeated initialization but does not prove ten is universally sufficient.

We retain the unfavorable original evidence. On the original Test extended to five seeds, MAPDP/MAPT gains are 1.90/2.82 pp; paired seed-t 95% CIs are [-0.12, 3.91]/[-0.04, 5.69], and both exact two-sided sign-flip p-values are 0.125. Thus the original tied/negative seeds and inconclusive seed-level tests are not superseded by the current result.

W2/Q2: What was inspected and what can be established

The original Test was used for quantitative development comparisons, beyond checking evaluation code. Retained records show:

Date (2026)Recorded evidence
September 20MAPDP Full/Pair-only/Route-only/No-PACF Test results and difficulty/hazard breakdowns were interpreted in a development report.
September 21A Validation diagnosis found unintended MAPT feedback on MOVE/WAIT; the correction restricted feedback to conditional target selection.
September 22Corrected MAPT was tested; route-input ablations were planned with reference to Test results.
September 23 onwardMAPDP execution-protocol alignment and retraining occurred after Test comparisons were available.

All 12 original checkpoint epochs match the reconstructed Validation rule: maximize rescue rate, minimize incapacitations, then select the earliest tied epoch. Selected epochs for seeds 1/2/3 were MAPDP Base 48/48/48, PACF 32/48/16; MAPT Base 16/16/8, PACF 48/64/48. This supports checkpoint selection, but cannot establish that design/hyperparameter choices were independent of Test exposure. The MAPT correction has direct Validation evidence; chronology alone does not prove Test caused it. We cannot reconstruct every informal decision.

We therefore treat the original Test as development-exposed retrospective evidence. The 60-building evaluation was frozen before its first results, with main available checkpoints fixed and a prespecified Validation rule for the still-running fixed-cost control. The subsequent ten-initialization protocol was fixed before its own results but reused those evaluated layouts; it is not a second untouched architectural holdout. Capacity and candidate-cap additions are exploratory. These evaluations do not erase the original exposure.

AuthorsOpenReview ↗

Planner fairness and problem formulation

W3/Q3: Common execution planner and search budgets

You identified a genuine confound: the original heuristic implementations used nominal shortest routes, while learned policies used risk-weighted routes. Nominal routing was an implementation convention, not a restriction of those allocators. Base/PACF pairs already shared their planner; the cross-family comparison required correction.

All results below use the same risk-weighted candidate planner (risk coefficient 2), minimum-cost route selection, legal masks, commitments, service rules, and environment-seed schedule on 600 scenarios (60 buildings × ten initializations). Weighted rescue uses difficulty weights 12:18:24. Neural models use five training seeds; stochastic planners use five search seeds; deterministic rules use one rollout per scenario.

MethodMedium (%)Hard (%)Expert (%)Weighted (%)
MAPDP Base99.7896.7689.0394.00
MAPDP + PACF99.8698.5093.0796.39
MAPT Base99.8096.6890.7394.73
MAPT + PACF99.9799.0393.3596.71
RMCA-adapted100.0098.0692.5996.06
Nearest99.8396.8388.1093.62
Hungarian99.8396.3988.4293.61
Risk Hungarian99.8396.9287.3893.32
SA, budget 6099.3487.8763.7379.69
GA, budget 6099.6592.5280.0388.55

Hungarian and Risk Hungarian differ in assignment costs (distance versus current risk-weighted cost), not execution planning. Risk-based assignment alone does not improve this aggregate result. Shared-planner Nearest/Hungarian/Risk Hungarian on the original 48 labels score 88.19/88.19/87.62%; comparing these with the new rows cannot isolate a planner effect because the evaluation sample changes.

We retain the original Medium counterexample (heuristics 100%, PACF 95.66%). Current Medium scores are near saturation, but that does not causally explain the original decline. Buildings and initializations both changed.

We also completed the entire search-budget grid, retaining all 18,000 episodes, including truncations:

Objective evaluations per solveSA mean (%)GA mean (%)
6079.6988.55
18077.2583.12
60078.6978.89

All 1,018,548 recorded solves respect their budgets and return the best objective encountered. The route-cost oracle matches execution, including fallback and same-room cases. However, the coverage-first nominal chain-cost objective does not predict future hazards or victim health. Of 2,379/2,076 SA/GA initial-state pairs with improved proxies at budget 600 versus 60, rescue outcomes are worse in 544/608. Better initial proxies need not yield better rescue. Even perfect rescue in every truncated budget-600 episode would give only 79.10/79.43%, below the budget-60 means. This is not an equal-wall-time quality comparison.

RMCA-adapted uses regret insertion and six LNS rounds from Chen et al., under common rescue execution rather than the original collision guarantees. PACF-minus-RMCA differences are 0.33 pp (MAPDP; conditional building CI [-0.48, 1.19]) and 0.65 pp (MAPT; [-0.23, 1.57]). Both include zero; we do not claim superiority over all planning methods.

M1: Notation

We distinguish routes ξijk\xi_{ijk} from rewards rnr_n, event ticks TtT_t from temperatures τA,τR,τP\tau_A,\tau_R,\tau_P, elapsed ticks Δnt\Delta n_t from edge duration cetimec_e^{\mathrm{time}} and hidden width dhd_h, and transition kernel P\mathcal P from victim set Ivic\mathcal I_{\mathrm{vic}} and pair count NpairN_{\mathrm{pair}}. These corrections do not alter the evaluated model.

M2: Partial observability and semi-Markov decisions

We agree: victim health is hidden from both actor and critic, and observed hazard trends need not form a sufficient belief state. The correct formulation is centralized partially observable control with variable-duration, semi-Markov decision epochs, not a fully observed MDP.

We verified duration-aware rewards rˉt=∑ℓ=0Δnt−1γℓrTt+ℓ\bar r_t=\sum_{\ell=0}^{\Delta n_t-1}\gamma^\ell r_{T_t+\ell} and bootstrap γΔntV(ct+1)\gamma^{\Delta n_t}V(c_{t+1}), where Δnt=Tt+1−Tt\Delta n_t=T_{t+1}-T_t. Duration correction does not recover hidden information. This clarifies the existing implementation; training is unchanged.

M3: Centralized control and communication

“Multi-agent” denotes the physical team. One coordinator trains and executes a joint policy; rescuer-conditioned factors are not independent local controllers. MAPDP factors are parallel; MAPT uses autoregressive conditioning. Globally shared current observations are not the full simulator state. Reliable observation/command delivery is an idealized assumption: communication loss, delayed messages, and decentralized perception have not been tested. We limit operational claims accordingly.

AuthorsOpenReview ↗

Controls, learned feedback, and novelty

W4: Contribution and interpretation

We agree that PACF is a learned route-conditioned logit bias and that the KL/soft-min identities are standard. The return argument requires an unmeasured calibration bound; it is not a guarantee for the trained policy, greedy rescue rate, or PPO convergence. “Consequence” denotes supervision through downstream team reward, not calibrated route-return or future-hazard prediction.

The contribution is an explicit executable-route-to-target interface before commitment in a rescue simulation platform. Coupling assignment and paths is not itself new. Bounded scores, normalized aggregation, and zero initial correction are PACF design properties, not proved advantages over simpler fusion.

Q4/W5: Route information versus capacity and integration

All controls use MAPT, common training seeds 1–3, 64 epochs/8,192 episodes, Validation-only selection, and the same 600 scenarios (60 buildings × ten initializations). Rescue is averaged within buildings and difficulty, with weights 12:18:24. ± is training-seed sample SD; CIs are conditional building-bootstrap intervals, unadjusted for multiple comparisons. Differences use unrounded values and are alternative minus PACF.

ModelRescue (%)Difference (pp)95% CI (pp)
PACF96.64 ± 0.660.00Reference
Base94.86 ± 1.08-1.77[-2.42, -1.11]
Route-free capacity control93.63 ± 2.41-3.01[-3.47, -2.55]
Ordinary route head97.02 ± 0.34+0.39[0.10, 0.69]
Fixed minimum-cost bias96.74 ± 0.22+0.10[-0.17, 0.39]

Ordinary uses the same route inputs/encoder architecture, independently trained weights, masked mean pooling, and a target-scoring MLP. PACF scores routes before aggregation. Ordinary initialization is random; PACF starts at zero feedback, so this does not isolate aggregation alone.

Active parameter counts are Base 223,677; PACF 594,170; Ordinary 594,298; capacity control 594,493, counting shared parameters once and excluding disabled branches. The capacity control adds a residual scorer from Base inputs only, without routes/history. Its result weakens a parameter-count-only explanation but does not equate function classes or optimization. It is an exploratory addition.

Fixed feedback uses Cij=min⁡kbijkC_{ij}=\min_k b_{ijk} and subtracts (Cij−μ)/σ(C_{ij}-\mu)/\sigma from target logits, with Train-only μ=4.16884\mu=4.16884, σ=2.14576\sigma=2.14576, coefficient one, and full dispatcher retraining. Ordinary exceeds PACF; fixed feedback has a higher mean with a CI containing zero, which does not establish equivalence. The evidence supports route information across integration designs, not unique superiority of PACF.

Input interventionRescue (%)Difference from PACF (pp)95% CI
Remove route tokens, retain relative statistics95.27 ± 1.38-1.36[-1.97, -0.81]
First hop + statistics96.55 ± 0.40-0.09[-0.40, 0.20]
Remove observed hazard trends96.16 ± 1.09-0.48[-0.69, -0.27]

The first/trend interventions lower the mean; first-hop results do not establish an additional benefit from complete routes or equivalence.

W5/Q5: What feedback learns and changes

A prespecified manifest-based sample of 12 scenes, two seed-1 models, and 24 trajectories yielded 4,472 joint decisions and 7,778 ticks. Instrumentation preserves archived actions/outcomes. Within decision/rescuer contexts, centered Pearson correlations with correction C are:

VariableMAPDPMAPT
Minimum planner cost0.7870.594
Candidate count0.3900.313
Mean route risk0.1770.104
Maximum route risk0.2340.165

Excluding invalid pairs, these visited-state correlations are not calibration or causal estimates. At fixed weights, observations, masks, and decoding prefixes, feedback changes the top target in 120/434 MAPDP contexts (27.65%) and 157/454 MAPT contexts (34.58%). All 5,439 selected routes remain minimum-cost choices.

For the earliest changed-target MOVE followed by rescue/handoff, both models switch from a third-floor to a ground-floor room at t=0; planner costs change 5.57→1.93 (MAPDP) and 6.30→1.93 (MAPT). Both routes have zero current risk. Service begins at 16 s, three victims are picked up at 18.9 s, and handoff occurs at 120 s. The next evacuation event contains one of them. This outcome-selected example illustrates target prioritization, not hazard avoidance or a closed-loop counterfactual benefit.

The original stair-pressure totals (+63 MAPT rescues, -9 MAPDP) remain reported. Extending the same original Test to five seeds gives mean gains +8.70/+2.31 pp, respectively; opposite signs are not stable evidence of a backbone-specific mechanism. Overlapping hazard strata and added seeds do not establish the cause of the original difference.

I would like to thank the authors for their response. I sincerely appreciate the effort that authors did to address the comments. However, the new results essentially state that the gains come from route information rather than from PACF’s design. The ordinary route head outperforms PACF, the fixed minimum-cost bias is on par with it, and PACF has no advantage over RMCA-adapted. The feedback mainly tracks planner cost rather than route risk, and the sensitivity study finds the best result with a single retained route (k = 1). I appreciate that these results are reported openly, but they leave little support for PACF as a methodological contribution or for the “consequence feedback” framing in the title.

I therefore keep my original evaluation for this paper.

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

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