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Under review as a conference paper at ICLR 2027

Regression Accuracy Is Not Enough: Destination-Agnostic Graph Embeddings for Potential-Field Navigation

Abstract

Potential-field navigation using destination-conditioned Graph Neural Networks(GNNs) requires a new forward pass whenever the target goal changes. To eliminate this per-goal computational bottleneck, we propose a destination-agnostic embedding framework. By executing a single forward pass per map, our model assigns a D-dimensional vector zi to each free cell such that the distance approximates the shortest path to an arbitrary goal, enabling instantaneous inference for any goal without retraining or additional forward passes. We train the network using a combined objective of pairwise distance regression and an order-preserving ranking loss. Model performance is evaluated on both distance-regression accuracy and task-level navigation success rate via greedy descent. Through extensive hyperparameter sweeps over ranking-loss weights (from 1000 down to 1) and anchor/pair sampling densities, we reveal that regression accuracy (Mean Squared Error, MSE) and navigation success are surprisingly decoupled: while MSE improves monotonically toward the smallest weight, completion rate and ranking correctness peak at an intermediate weight. Thus, the configuration that minimizes regression error fails to maximize navigability. We trace this phenomenon to specific map topographies—including cases where completion rate remains unchanged despite substantial MSE improvements—and attribute it to structural limitations of symmetric embeddings in greedy goal-reaching. Our findings demonstrate that regression error alone is an unreliable proxy for downstream planning success, highlighting the need for future evaluation protocols to report task-level navigability alongside embedding accuracy.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Destination-Agnostic Graph Embeddings, Potential-Field Navigation, Graph Neural Networks, Ranking Loss, Task-Level Navigability, Path Planning

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.
Reviewer_6sDVOpenReview ↗
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Paper summary

In this manuscript, the authors propose a destination-agnostic Graph Neural Network (GNN) to solve the potential-field navigation problem without target conditioning. In particular, their model maps each cell of an occupancy grid to an embedding z_i, aiming to approximate the shortest-path distance for any possible goal. The paper’s main claim is that evaluating and training such models relying only on MSE (regression accuracy) is not a suitable proxy for greedy-descent navigability. The authors further support their claims in the experimental section with a map-level study and argue that the regression objective itself does not enforce the local monotonicity that greedy descent requires.

Critical strengths
  1. The experimental setup and training details are carefully reported throughout the paper, and the attached supplementary material is easy to follow.
  2. Overall, the research question about single-forward-pass embedding generation to solve the proposed problem in a conditioning-free setup is reasonable.
Critical weaknesses
  1. Clarity, style, and writing concerns: overall, the presentation is poor and below the venue’s standards. Manuscript sections are poorly written and below the expected level of clarity. From the beginning, the paper’s scope is not clearly framed, and the writing style seems to continuously overstate the work’s merit without getting straight to the point, leaving a sense of vagueness (e.g., lines 314-315 for limited experimental evidence). The paper’s narrative is oddly interrupted by experimental setup description, implementation or file formatting details, or inline math describing the model’s architecture; while reproducibility and clarity are a fundamental part of a manuscript, I think that these details belong in the appendix. Finally, the figures are not ready for publication and only drafted (Figure 1 has matplotlib's colorbar only attached on the rightmost panel, and Figure 2 subplots titles are barely readable). I strongly suggest that the authors thoroughly revise the manuscript’s style before publication.

  2. Limited related work section. The bibliography is scarce and omits whole lines of research in the field, ranging from relevant research on neural planning on grids (e.g., Yonetani et al., Path Planning using Neural A* Search, ICML 2021) to an analysis of current GNN applications in this area (e.g., Veličković et al., Neural Execution of Graph Algorithms, ICLR 2020). Engaging with the relevant literature would strengthen the novelty and better position the paper.

  3. Limited novelty and weak experimental setup. Although an original application of GNNs could potentially be of relevance and interest to the community, this manuscript only presents an incremental contribution, proposing a method that only “assembles” existing components in a naive way: GATv2 as the GNN backbone, P-GNN-inspired distance supervision, and a standard contrastive loss (pairwise ranking). Beyond the incremental formulation of the methodology, the main claim that “regression accuracy is not planning success” has already been established in the literature and recognized by the community (see, for example, Chrestien et al., Optimize Planning Heuristics to Rank, not to Estimate Cost-to-Goal, NeurIPS 2023, for a broad treatment of the problem). Here, the authors do not propose a novel theoretical or methodological perspective on this known problem, strongly limiting the novelty of the overall work. Finally, the experimental setup is narrow, testing the authors' method only in a synthetic scenario, without statistical analysis (30x30 maps, 50 test maps) and providing no external baselines to support the paper's claims.

Questions for authors
  1. Novelty: How does this work contribute beyond existing literature?

  2. Statistics: Can authors provide a significant statistical assessment of their methodology?

  3. Baselines: After having addressed 1 and 2, can the authors provide and compare against multiple external baselines?

2 comments
AuthorsOpenReview ↗

Response to Reviewer 6sDV

Thank you for the detailed review. We answer the three questions first and then the writing, figure and related-work points.

Novelty. We agree that the broad point that cost-to-goal regression is not what a planner needs is known: Chrestien et al. (NeurIPS 2023) argue this for learned heuristics in A* and greedy best-first search and propose ranking losses for them. We do not claim this point as new, and the revised introduction and Related Work say so. Our setting differs in two ways. (a) We learn a goal-agnostic embedding that is computed once per map, and the potential field for any goal is obtained afterwards as an embedding distance; greedy descent on this field then requires local monotonicity at every cell on the path, not a good expansion order. (b) We quantify, for this setting, how far regression error and descent success are coupled (Spearman -0.35 over 20 runs, with differences between loss weights and sampling densities falling inside seed noise) and localise where descent fails. We have added the Neural A* line of work (Yonetani et al., ICML 2021) and Chrestien et al. to Related Work, and Neural Execution of Graph Algorithms (Velickovic et al., ICLR 2020) as a neighbouring use of GNNs on graph algorithms; we state plainly that our architecture is an assembly of existing components and that the contribution is the empirical analysis, not the architecture.

Statistics. The submitted version reported one seed. We have since trained the main configuration with 11 seeds and report mean and standard deviation: completion 92.46 +/- 0.57%, MSE 826 +/- 63, ranking violation 5.97 +/- 0.12% (seed 42, as in the paper: 93.07%, 774, 5.77%). For the comparison configurations (rank_weight 1; 32x128 sampling) we trained seeds 0-4 and report seed-paired differences with t-statistics and map-level bootstrap intervals. The conclusion changes: differences between configurations in completion rate are within seed noise (for example -0.20 pp, map-level 95% interval [-0.82, +0.26], for rank_weight 1 vs 10), and we have removed the claim that completion peaks at an intermediate weight. Per-map completion distributions are reported as well (10 of 50 maps always solved; the worst 10 maps carry 66% of failures).

Baselines. The in-framework baseline is the goal-conditioned regressor (3 seeds); we report its best setting (mono_weight 3) and make no claim about a sweep. We have not added external planners in this revision. Neural A* and similar methods solve a different problem (they learn a guidance map for a search from a given start and goal), so they are not directly comparable to a precomputed goal-agnostic potential field evaluated by greedy descent. A fair comparison would use our learned field as the heuristic inside A* or GBFS, which we list as future work together with landmark-based non-learned embeddings. We have added this to the limitations section.

Clarity. We moved implementation and file-format details from Sections 4-5 into the appendix, shortened the overstated phrasing in the introduction and conclusion, and replaced the failure-map figure with one that has a single labelled colourbar and no baked-in titles. We also corrected the metric definitions in Section 5.3 so they match the evaluation code, and replaced phrases that referred to the submission history with plain statements of the current results.

Figure 1 of the submitted version (Figure 2 in the appendix of the revised paper): the train and test map panels. The train-map panel shows a colour field only because the same plotting routine renders both map files, and every map file stores a goal and a field. Training maps are used only through anchor-target pairs; the stored goal and field are never read, so the colour on the train map carries no information and has no scale to share. Only its obstacle layout matters. We have corrected the caption to say this, so the two panels are not read as sharing a meaningful colour scale; the colour and colourbar apply to the test map, whose goal and field are the evaluation target.

I thank the authors for the detailed response and revised experiments, that addressed some of my concerns. However, the revision still presents the incremental contribution I highlighted in my initial review. I therefore cannot recommend the acceptance of the manuscript in its current form.

Reviewer_ctbqOpenReview ↗
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Paper summary

The paper targets path planning and navigation tasks. It uses graph embeddings to approximate shortest-path distances and then treats the embedding distances as potential values for local greedy navigation. The model feeds the 8-neighbor grid graph structure of the map and normalized node coordinates into GATv2, generates vectors for all traversable nodes in a single forward pass, and can reuse these representations when the target changes. Training uses BFS shortest-path distances on the 4-neighbor graph as labels, fits the distances with an MSE loss, and applies a ranking loss under the same anchor to constrain the relative distances between nodes. During navigation, the model selects the neighbor with the smallest embedding distance to the target and terminates when no neighbor has a lower potential value. All experiments are based on 30×30 synthetic grids, with 1,000 training maps and 50 test maps. The paper compares distance error and navigation completion rate under different ranking weights and sampling densities, and also compares against a target-conditioned model. The results show that for some configurations, MSE decreases while the completion rate also decreases, and that the parameter settings achieving the lowest error and the highest completion rate are different. Although the target-conditioned baseline has lower MSE, its completion rate is substantially lower than that of the better configurations of the proposed method. The authors therefore argue that distance regression accuracy is not a sufficient proxy for greedy navigation performance and summarize this inconsistency as a “decoupling” of the two types of metrics. In addition, through failure cases, the authors discuss possible structural limitations of symmetric embeddings for greedy navigation. The paper concludes by emphasizing that when evaluating navigation-oriented graph embeddings, both task-level reachability and embedding accuracy should be considered.

The problem raised by the paper is valuable, but the methodological novelty and experimental validation are not yet sufficient. Its main technical components already have clear foundations; the new content mainly combines map representation reuse, distance supervision, and greedy navigation, and observes within this framework that distance error and completion rate do not vary consistently. The experimental setting is currently a bit simple, only small-scale synthetic maps are covered, each test map uses only one target, and performance on other map types and with different target positions has not been sufficiently validated. Some key differences in completion rate are small, while the main method reports results from only a single random seed, making it difficult to judge whether these small differences are stable. The model structure supports cross-target reuse, but the actual efficiency gain is not quantified. Regarding the mechanistic explanation, the distinction between global distance fitting and the local descent condition is reasonable; however, the current evidence is insufficient to determine whether symmetric embeddings are the main cause of navigation failures.

Critical strengths

The problem addressed in this paper is of some value, and sharing the map encoding across multiple targets also has clear practical significance. By combining parameter studies with failure cases, the paper discusses the decoupling between distance prediction and actual navigation performance, which is a relatively distinctive finding. This gives the paper both a concrete methodological implementation and a discussion of evaluation metrics and failure causes.

Critical weaknesses

The incremental methodological contribution is not sufficiently demonstrated. The main components—GATv2, distance regression, fixed-margin ranking loss, and decoupling representation from goal query—have clear precedents. Combining map encoding reuse, shortest-path distance supervision, and greedy navigation is practically meaningful, but it remains largely an integration of existing ideas for the navigation task. The more independent contribution is the empirical observation that distance error and navigation completion rate can decouple, yet this is currently validated only under one encoder, one synthetic map distribution, and one greedy navigation strategy.

The experimental scope is too narrow to support general conclusions. All experiments are confined to 30×30 synthetic 2D grids with randomly generated convex disk-like obstacle clusters. There is no evaluation on standard pathfinding benchmarks, real indoor robot grid maps, or mazes with long loops and dead ends. The paper also does not systematically control or report coverage of narrow corridors, U-shaped obstacles, or complex bottlenecks. The authors’ own test_map_0041, where the goal lies in a local narrow passage, has a completion rate of only 73.44%–75.96% across compared configurations. Since the full distribution of per-map completion rates is not reported, it is difficult to rule out that high completion rates on easy maps inflate the average and mask weaker performance on complex structures.

The statistical evidence for the central empirical claim is weak. The test set contains only 50 maps, and the main method reports results from a single random seed (seed=42) without mean±std or confidence intervals. Some key differences are very small: under the 16×64 setting, changing rank_weight from 10 to 1 reduces MSE from 774.42 to 764.15, while completion rate changes only from 93.07% to 92.71%—a 0.36 percentage-point difference. Similarly, increasing sampling density from 16×64 to 32×128 reduces MSE from 774.42 to 746.27 but changes completion rate from 93.07% to 92.66%, only 0.41 percentage points. Without repeated training, these differences cannot be distinguished from sampling or training noise, and interpreting them as evidence of an intrinsic tension is premature.

The cross-model comparison is confounded. The target-conditioned baseline differs from the proposed method in input information, representation constraints, and supervision. Although the baseline has lower MSE but substantially lower completion rate, this mainly shows that metric rankings can differ across two different models; it does not establish that the regression objective itself misleads navigation. Moreover, Table 3 reports only one averaged baseline setting, so the claim that the decoupling also appears in target-conditioned models is not fully supported by a complete baseline sweep.

Important ablations on representation capacity and message-passing range are missing. The main experiments fix embed_dim=16 and num_layers=4. A four-layer GATv2 explicitly aggregates information from only a four-hop neighborhood in the 8-neighbor graph, whereas the task requires predicting global shortest-path distances. Normalized coordinates provide spatial position but do not directly tell the model whether a distant obstacle must be circumvented. The paper should vary embedding dimension and propagation range to determine whether the observed phenomenon persists and to rule out representation capacity or information-range bottlenecks.

The failure mechanism is not directly validated. The explanation that average distance error can decrease while local ordering errors remain is plausible, but the paper does not visualize predicted potential fields on failed trajectories or quantify which local errors cause failures. The ranking loss compares distances from the same anchor to two sampled nodes, which are not necessarily adjacent; therefore, it does not directly guarantee that the current position has a traversable neighbor with lower potential. Table 3 further shows that the target-conditioned baseline has the lowest ranking violation rate (5.41%) but a clearly lower completion rate, indicating that a lower global ranking violation rate does not automatically imply better greedy navigation. Direct statistics on non-goal nodes lacking a descending neighbor, local traps affecting start states, and changes in these errors under different ranking weights are needed.

The claimed benefit of multi-goal reuse is not experimentally supported or quantified. Although the model structure allows node representations to be reused when the goal changes, each test map uses only one fixed goal. The paper does not evaluate multiple goals per map or analyze performance when the goal is near dead ends, narrow entrances, or obstacles. It also does not report actual latency, memory usage, or total cost as a function of the number of goal queries. The reduction in forward passes is a valid structural advantage, but the practical speedup and the number of goal queries needed to realize it remain unquantified.

Overall, the decoupling observation is interesting and potentially useful, but the current evidence relies on a narrow synthetic setting, small metric differences without repeated-training variance, limited ablations, and an explanatory failure analysis that has not yet been directly verified. These issues limit the strength and generality of the paper’s main conclusions.

Questions for authors

Please see the weaknesses part.

2 comments
AuthorsOpenReview ↗

Response to Reviewer ctbq (Part 1)

Thank you for this careful review. The numbers you quote are right, and they motivated the new experiments below.

Statistical evidence. You are correct that single-seed differences of 0.36 pp (rank_weight 10 vs 1) and 0.41 pp (16x64 vs 32x128) cannot be interpreted. We retrained the main configuration with 11 seeds (completion 92.46 +/- 0.57%, MSE 826 +/- 63; seed 42 gave 93.07%, the second best of 11) and both comparison configurations with seeds 0-4. Paired by seed: rank_weight 1 vs 10 gives MSE +5.5 (t=0.22), completion -0.20 pp (t=-0.69), ranking violation +0.12 pp (4 of 5 seeds; not significant, p=0.13); 32x128 vs 16x64 gives MSE -51.8 (t=-2.4), completion -0.20 pp (t=-0.68). Map-level bootstrap intervals for completion include zero. We therefore removed the claim of an intrinsic tension and the claim that completion peaks at an intermediate weight. The supported claims are that completion does not differ detectably between the compared settings of these two hyperparameters (rank_weight 1 vs 10; 16x64 vs 32x128), and that MSE and completion are only loosely coupled (Spearman -0.35 over 20 runs).

Per-map distribution. Averaged over the 11 seeds, 10 of 50 maps are always solved (100%) and 7 are below 80% (worst: map 18 at 61%; map 41 at 74.8%). The worst 10 maps carry 66% of all failures, so your concern is justified: the average hides a heavy tail. We now report this distribution, and we restrict the claims to the tested distribution.

Cross-model comparison. We agree. The goal-conditioned model differs in input, constraints and supervision, so the comparison shows that metric rankings can differ across two models, not that the regression objective misleads navigation. We have rewritten Section 6.3 accordingly. In the revised paper the baseline appears in Table 1(c) at its best setting only (mono_weight 3, mean of 3 seeds), and we make no claim about other settings.

AuthorsOpenReview ↗

Response to Reviewer ctbq (Part 2)

Failure mechanism. We now measure it directly. We extract every non-goal local minimum (a cell with no strictly lower neighbour), its basin (the number of start cells that descend into it), and its location. Each model has 34-49 such minima over the 50 test maps; the large ones (basin of 50 cells or more) are 16-23. Pooled over the 11 seeds there are 82 distinct (map, cell) minima; 36 occur in at least 6 seeds and account for 89% of all failing starts, and 71% of the distinct failing (map, start) pairs fail in at least 6 seeds. Changing the ranking weight does not remove them: with rank_weight 1 (seeds 1-4) there are 38.5 minima on average vs 39.8 for rank_weight 10 on the same seeds, and 93-100% of them are at cells already seen in the baseline seeds. They concentrate at concave, obstacle-adjacent positions that require a detour (every one has at least 3 of 8 neighbours blocked; detour ratio and concavity at about the 95th percentile of same-map cells at similar hop distance). We also agree that the pairwise ranking loss does not guarantee a lower neighbour. We therefore trained with an additional loss that requires every non-goal cell to have a lower-valued neighbour (weights 0.3-10, seeds 0, 1): completion stayed within about 1 pp of the baseline and 92-100% of the minima remained at the same cells. Together with the weak coupling above, this supports a structural limitation, but it does not isolate symmetry as the cause, and we now label that explanation a hypothesis.

Representation capacity and message-passing range. We did not vary embed_dim or num_layers in this revision, so we cannot rule out a capacity or range bottleneck. We say so in the limitations; note that the descending-neighbour experiment above also did not help at the same capacity.

Scope and multi-goal reuse. All maps are 30x30 synthetic with convex clusters, and each test map has one goal. We agree this limits generality, and we have narrowed the claims to this distribution. The reuse benefit is structural (one forward pass per map instead of one per goal); we have not measured latency or memory, and we state this explicitly rather than claim a speed-up.

Reviewer_fvnGOpenReview ↗
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Informativeness
2
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Paper summary

The paper proposes a destination-agnostic embedding GNN with anchor-based regression.

The contribution is not much.

The fact that MSE and completion are orthogonal is a good find, but not very surprising or useful.

Critical strengths

The paper makes a good contribution, that of destination-agnostic embedding GNN with anchor-based regression.

It also empirically establishes that there is little connection between regression accuracy and completion accuracy.

Critical weaknesses

The choices made in the Method section does not explain the intuition or rationale behind them.

Only synthetic maps and no real data have been used for experiments.

Findings are specific to map distributions tested. How likely are they generalized?

Questions for authors

Can the graph not contain any cuts or obstacles in the map?

What is a better proxy for completion accuracy since MSE is found to be largely orthogonal?

Can embeddings be learned with the additional constraint of preserving local consistency?

2 comments
AuthorsOpenReview ↗

Response to Reviewer fvnG

Thank you for the review and the three questions.

Q1: Can the graph contain no obstacles, or cuts? Every training and test map has obstacles (20-30% density, convex clusters). We have not evaluated obstacle-free maps; since the failures we localise sit at concave, obstacle-adjacent detour positions (every local minimum has at least 3 of 8 neighbours blocked), we expect them to be rare there, but we have not tested this. For graphs with cuts (disconnected free space): during training we sample targets only among cells reachable from the anchor, so disconnected components are handled, but all test maps were generated so that every free cell can reach the goal, and goals in a different component are not evaluated. We state both in the limitations.

Q2: A better proxy than MSE. Two proxies, both computed on our 50 maps. (i) The ranking-violation rate is a weak proxy: Spearman -0.24 with completion over 20 runs, and the goal-conditioned baseline has the lowest violation rate (5.41%) with a much lower completion rate. (ii) Counting large-basin non-goal local minima tracks completion closely: Spearman -0.92 between completion and the number of minima with a basin of 50 cells or more across the 11 main-configuration seeds (-0.67 with a 20-cell threshold). Part of this relation holds by construction, because a local minimum is itself a failing start, so we recommend it as a localisation tool, not as an independent validation: it shows where descent breaks, from one embedding, and which cells recur across seeds. Q3: Can embeddings be learned with a local-consistency constraint? We tried it. In addition to regression and ranking, we added a hinge loss requiring every non-goal cell to have a neighbour with lower predicted distance to the anchor. With weights 0.3, 1, 3, 10 (seeds 0 and 1), completion stayed within about 1 pp of the baseline, and 92-100% of the local minima remained at the same cells. An earlier variant that penalised local monotonicity along anchor-to-target paths reached only about 65% completion (Section 8). The loss supervises only the fixed anchors, so this negative result does not exclude other ways of enforcing local consistency. We report it in the revised paper.

"MSE and completion are orthogonal." Thank you; with 11 seeds we can be more precise: the two are weakly coupled (Spearman -0.35 over 20 runs), and the differences between loss weights and sampling densities in the original Table 3 fall within seed noise. We have rewritten the claims accordingly. We also agree the contribution is modest: our architecture assembles existing components, and the contribution is the empirical analysis of when regression accuracy fails to predict descent success.

Rationale for the method choices. We have added one sentence of rationale to each design choice in Section 4: coordinates-only inputs so that no destination information leaks; 8-neighbour message passing to match the agent's moves; 4-neighbour labels to define the ground truth; and a fixed-margin ranking loss with a large weight because the raw regression term has a scale of hundreds.

Synthetic maps and generalisation. We agree that only synthetic 30x30 maps are used and that the findings are specific to this distribution; the test density (25%) lies inside the training range (20-30%) and we have not evaluated other distributions. We restrict the claims to the tested distribution and list real maps and other map families as the main open limitation.

Reviewer_fvnGOpenReview ↗

Acknowledge

I acknowledge the responses from the authors. This has made the paper clearer.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response

We thank all reviewers. The most common concerns were (i) a single random seed with small metric differences, (ii) a narrow synthetic setting, and (iii) weak evidence for the failure mechanism. Since submission we retrained the main configuration with 11 seeds (seed 42 plus seeds 0-9) and two comparison configurations (rank_weight 1; 32x128 sampling) with seeds 0-4, and analysed failures at the level of individual local minima. We will upload a revised PDF.

  1. Seed 42 was an optimistic seed. Main configuration, mean ± std over seeds: completion 92.46 ± 0.57%, MSE 826 ± 63 (n=11). Seed 42 reached 93.07%, the second highest of 11 runs.
  2. The Table 3 differences are within seed noise. Paired by seed (0-4): rank_weight 1 vs 10 changes MSE by +5.5 (t=0.22) and completion by -0.20 pp (t=-0.69); 32x128 vs 16x64 changes MSE by -51.8 (t=-2.4) and completion by -0.20 pp (t=-0.68). The only visible effect is ranking violation, +0.12 pp at rank_weight 1 (4 of 5 seeds; not significant in the 5-seed test, p=0.13). We therefore withdraw the claims that completion peaks at an intermediate weight and that MSE is minimised at the smallest weight. The supported statement is weaker: within the tested range completion does not differ detectably between rank_weight 1 and 10 or between 16x64 and 32x128 sampling, and MSE and completion are only loosely coupled (Spearman -0.35 over 20 runs). The gap to the goal-conditioned baseline (MSE 578 vs 826, completion 81.3% vs 92.5%) is much larger than seed variation.
  3. Failures come from a few recurring local minima. Per-map completion is far from uniform: 10 of 50 maps are always solved, 7 maps stay below 80%, and the worst 10 maps account for 66% of all failures (worst 20: 93%). Each model has 34-49 non-goal local minima over the 50 test maps (cells with no lower neighbour). Pooled over the 11 seeds there are 82 distinct minima; 36 of them occur in at least 6 seeds and account for 89% of all failing starts, and the local minima of the rank_weight 1 models lie at cells already seen in the baseline seeds (93-100%; 69-89% at cells recurring in at least 6 of 11 baseline seeds). They concentrate at concave, obstacle-adjacent detour positions (every one has at least 3 of 8 neighbours blocked; detour ratio and concavity both at about the 95th percentile of same-map cells at similar hop distance).
  4. Directly training for local consistency did not help. We added a loss that requires every non-goal cell to have a neighbour with lower predicted distance. With weights 0.3-10 (seeds 0, 1) completion stayed within about 1 pp of the baseline and 92-100% of the local minima remained at the same cells. We now present the symmetric-embedding explanation as a hypothesis, not a finding.
  5. Corrections. We aligned Section 5.3 with the evaluation code: the ranking-violation rate is computed over adjacent 8-neighbour pairs whose true field strictly increases; MSE is computed over the fixed-goal field on all free cells; completion is measured from every free cell.
  6. Remaining limitations (now stated explicitly). All maps are 30x30 synthetic, each test map has one goal, we compare against one goal-conditioned baseline only, and we have not measured wall-clock savings of embedding reuse.

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

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