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Under review as a conference paper at ICLR 2027

Bidirectional Path Kernels for Local Split and Merge Detection in Policy Rollouts

Abstract

Offline policy rollouts can pass through the same local context and then follow several outgoing routes, or arrive there along several incoming routes, and neither endpoint dispersion nor a forward-only conditional law identifies this directed, path-valued object. We introduce the bidirectional local path-transition kernel (BLPTK): forward and reverse conditional laws of relative path segments, localized around a state–time context. At a declared path scale, minimum route mass and conductance tolerance, a spectral routine proposes partitions and an explicit mass-and-conductance test validates them, so every accepted partition certifies an empirical lower bound K+ or K- on outgoing or incoming path multiplicity — failure to accept one has no converse interpretation. No global route labels or annotated event times enter the detector. We want these junctions located because they are where reinforcement fine-tuning quietly deletes a route, and a local partition of them is something a training objective can be constrained against. On controlled directed graphs, path features classify all 361/361 probed local graph types, versus 255/361 for endpoint features on identical anchors. Across the round-two valency sweep, orthogonally embedded routes are counted exactly at full valency (1.000 from valency 2 to 8 and at 12, 0.994 at 10), with a false-positive rate of 0.091 traced to a grader–estimator threshold mismatch; crowded embeddings fail in three separable ways, including miscounted anchors of intermediate truth, a term exactness and recall are blind to. On D3IL-Avoid diffusion-policy rollouts the forward detector recovers the branchable contexts against a withheld label it never sees (AUROC 0.874 over 300 anchors, base rate 0.387); every trajectory there branches at the same moment, so a clock is optimal by construction and we report the measurement it cannot explain — within a fixed time slice, AUROC 0.879 over 220 anchors. On a simulated 7-DoF arm whose obstacle, and therefore whose junction time, moves between episodes, a clock is no longer optimal (max_t p(t)=0.410) and the detector leads the per-slice oracle clock by +0.260 agreement over 204 anchors. Freezing those outgoing regions as a deliberately naive branch-mass constraint during reinforcement fine-tuning keeps both demonstrated routes in all five seeds and passes a predeclared gate in four, where unconstrained fine-tuning deletes one in all five and, at matched dose, fixed-time regions and fork-window KL pass in zero — a probe of whether the regions are useful, not a proposed algorithm. Time reversal matches the forward count on all 204 matched balls, validating the reverse code path but giving no independent evidence for natural merges. Throughout, "certificate" means empirical partition feasibility at a declared resolution — not a confidence bound, and not recovery of a population route graph.

Primary area:
learning on time series and dynamical systems
Keywords:
policy rollouts, trajectory multimodality, split and merge detection, spectral clustering, conductance, path-space kernels, reinforcement learning fine-tuning, mode collapse, imitation learning, robot learning

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_oRXkOpenReview ↗
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1
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Paper summary

This paper proposes the Bidirectional Local Path-Transition Kernel (BLPTK), which uses the forward and reverse conditional distributions of local trajectory segments to identify local multi-path structures such as splits and merges in policy rollouts. The method first generates candidate partitions through spectral clustering, then explicitly validates them using mass and conductance criteria, and finally uses the resulting regions to impose a path-diversity constraint during reinforcement learning fine-tuning. Experiments cover synthetic graph structures, D3IL-Avoid, and a simulated 7-DoF robotic manipulation task.

Critical strengths
  • The paper clearly distinguishes outgoing splits from incoming merges, and points out that endpoint-based or forward-only information is insufficient to fully characterize such directed local path structures. The research question itself is clearly defined.
  • The authors specifically compare against a time-only clock baseline and same-feature clustering baselines, and explicitly report cases where BLPTK is outperformed by other methods rather than avoiding negative results.
  • In the simulated robotic task, constraining branch mass using the frozen local partitions preserves both demonstrated routes across five seeds, showing that the detected structures have at least some downstream utility.
Critical weaknesses
  • The main components of BLPTK, including conditional kernels, kernel regression, normalized spectral clustering, and conductance tests, are all based on existing techniques. The authors also explicitly acknowledge that they do not introduce a new transition operator, coherent-set decomposition, or statistical theorem. The main contribution therefore appears closer to a specific combination of existing tools together with a reformulation of the problem.
  • Across the 14 controlled cells, BLPTK is tied for the best result in only 5 cases and is outperformed by other methods in the remaining 9. In addition, in 9 of the 14 settings, its difference from the bare eigencount baseline is no more than 0.005.
  • The downstream evaluation contains only one simulated 7-DoF task, one geometry, and five seeds, and does not compare against existing diversity-preserving approaches such as trajectory entropy, mutual-information objectives, mixture policies, or behavior-regularized RL.
  • The references contain clear formatting and completeness issues. For example, Ref. [19] starts directly with the paper title and omits the author information. Conference names are also presented in inconsistent formats, including “International Conference on Learning Representations,” “ICLR,” “ICML,” and “IJCAI,” and the bibliography is not consistently formatted.
  • Most of the experiments are placed in the appendix. Based on the main paper alone, it is difficult to independently assess whether the method actually outperforms the baselines, under which conditions it fails, and whether the results are stable.
  • The template also appears not to follow the standard ICLR 2027 format. For example, the font differs from the Times-style font used by the official template.
  • The title and first-level section headings also do not match the small-caps style of the official template.
Questions for authors

See Weaknesses.

2 comments
AuthorsOpenReview ↗

Response to Reviewer oRXk (1/2): the formulation (W1) and the toy comparison (W2)

Thank you for the review. New results below were declared before they ran.

W1 (combination of existing tools). We agree that every component is standard, and that the contribution is a reformulation of the problem. That reformulation is what we propose: where a set of rollouts divides and rejoins, posed on a pair of directed local path laws and read out as counts at a declared resolution. The revised paper adds a single schematic of this formulation as Figure 1 (page 3): the forward and backward path laws at an anchor, the count read from them, and fine-tuning posed as a constraint on the same kernels at the detected regions. The same estimator on the same anchors classifies 361/361 probes with path features and 255/361 with endpoints. A discrete-time process is specified by its initial law and its conditional laws given the past. A policy is a probability kernel from its available information to actions; for a Markov policy that information is the state, augmented with memory or history when required. Together with the dynamics and the start distribution it induces a law over paths, regardless of whether its action density is tractable. Our object is that induced law at the level of local behaviour, namely the distribution of a path feature given the local context, in each direction. These conditional path-feature kernels generally depend on the policy parameters, including through rollout occupancy. At contexts where conditioning is well defined, a fixed measurable partition therefore defines policy-dependent masses; their gradients require differentiability and justification for differentiating the conditional expectations. These laws provide a natural object for comparing local behaviour across policies. Given samples from that law, single linkage uses only their pairwise distances and the total mass of each block, so it is one possible readout of the empirical kernel. The kernel is the more general object because it also supports readouts that depend on how probability is distributed within a connected set of paths, such as conductance. Here conductance refers to the graph induced by the declared affinity and path law, not to the policy's transition probabilities. A new test, declared before it ran, shows what this means on real rollouts. The cloned arm policies leave both routes in 9 to 15% of rollouts, and these strays run between the routes. Growing the rollouts sixteenfold, on anchors that are two routes at both sizes, single linkage's detection falls from 0.61 to 0.04, while the readouts that use probability, ours and DBSCAN with a mass threshold, roughly halve. Ours also fails the stability gate we declared, because at our tolerance of 0.005 the strays eventually make the route split too leaky to accept. We claim this generality only for what the object can express; on detection accuracy, strong clustering baselines on the same features are close on the arm and can be substantially more accurate on the toys. Single-linkage regions also pass as many seeds downstream, so this comparison establishes no downstream advantage specific to the BLPTK estimator. The revised paper makes the link to fine-tuning explicit: reward maximisation subject to preserving local kernel masses at regions detected from base rollouts, with the gradient of such a mass stated and proved, and the sense in which our penalty is only a biased surrogate stated beside it. This differs in kind from Behavioral Mode Discovery, which conditions a steering policy on a latent throughout and adds an information reward, with no step that locates regions. We also compare the kernels of two policies directly, with no partition. That map shows where plain fine-tuning changed behaviour, including at contexts where the count did not change, though our declared test fails for the constrained policy, whose change stays near the noise floor at this sample size. How best to use detected regions remains open, and our penalty is a naive first probe.

W2 (5 ties, 9 losses, 9 of 14 within 0.005 of the eigencount). These numbers are correct, and we do not argue for the method on accuracy. Some context on the toy cells: two have no branchable anchors, so a constant predictor scores perfectly there, and BLPTK beats that predictor in the other 12. The toy truth is a single-linkage count, so agglomerative clustering is graded by its own algorithm, and BLPTK ties for best in most staggered cells. This metric does not score what is specific to our estimator, the acceptance test that returns a feasibility witness. Every method in these cells also runs on our local directed path features at the declared resolution, so the cells compare readouts within the formulation. We test the formulation itself against endpoint features on identical anchors: path features classify 361 of 361 probes, endpoints 255.

AuthorsOpenReview ↗

Response to Reviewer oRXk (2/2): baselines (W3), presentation and formatting (W4–W7)

W3 (one task, no comparison with existing diversity methods). One task, one geometry and five seeds remain true for the RL result, and the revised paper says so. The downstream probe is there to show that the formulation can be used, by a plain penalty on detected regions. We do not offer it as a new diversity method. We ran the families you name where we could, end to end, reading reward first, because a policy that stays near behaviour cloning keeps its routes without fine-tuning. Behaviour cloning itself fails our gate on collisions in every seed.

  • Behaviour-regularised RL, full-policy KL to the cloned policy: doses 1, 0.3, 0.17 and 0.1 pass 0, 0, 0 and 2 of 5 seeds, against 4/5 for the local constraint. At dose 0.1, the closest in reward, its mean minority share among on-route rollouts is 17% against 37% for ours. Run to 3200 iterations, KL at dose 0.3 passes 1/5 and keeps 39% of the reward gain, where the local constraint passes 5/5 and keeps 79%. We make no claim about untried doses.
  • Trajectory entropy: an unlocalised bonus on whole paths passes 4/5 at dose 0.3 and diverges at doses 1 and 3. With a 3200-iteration minimum and the same stopping rule, both it and our constraint pass 5/5. Entropy keeps the routes more even (minority share 0.46 against 0.32) and ours keeps more of the reward gain (0.79 against 0.69). Neither dominates, and this comparison does not show that localising is what helps.
  • Mutual information: a DIAYN-style head on the diffusion policy passes 0/5 at doses 0.3, 1 and 3. In our first runs the declared validity check failed (discriminator accuracy 0.26 to 0.30 at the end of warm-up, chance 0.25). We then declared and ran a second version with a warm-up four times longer, run to convergence. Its discriminator identifies the four-way latent perfectly in all 15 runs, and every run still ends on one route while keeping 0.97 to 1.02 of plain fine-tuning's reward gain on average across doses. The warm-up left only 20 to 46% of rollouts on a route; we did not measure which features identified the codes. This is one implementation on one task, but it is a valid test, and it did not keep the routes.
  • Behavioral Mode Discovery: we reimplemented it from its paper, as we could not find released code. The paper uses two-step DDIM, deterministic for the frozen policy and stochastic during fine-tuning. Deterministic short-step sampling leaves the routes on our arm, so we used a stochastic 10-step sampler in both stages, which is a departure from it. The discriminator stayed near chance at the end of discovery, failing the same declared check. This is an attempt we could not make work on this arm, and we do not count it as a result against that method.
  • Mixture policies: we report no mixture baseline, because we found no published fine-tuning method of that form to reproduce.

These objectives act on the policy over all states, and none of them says where a rollout set divides or rejoins. That statement is what the formulation provides, and a detector can supply it for any of them. We do not show that using it improves on them.

W4, W6, W7 (references, font, small caps). You were right. Our build silently substituted the font and dropped the small caps. The revision uses the official style with a Times face and a consistent bibliography.

W5 (experiments in the appendix). The rebuttal limit is 10 pages. The revision moves the claim map and a compact downstream table into the main text, and adds a schematic of the formulation as Figure 1. The natural-merge results are in the main text, with their rollout figure in the appendix (Figure 5).

Reviewer_cEN9OpenReview ↗
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Paper summary

This paper proposes the Bidirectional Local Path-Transition Kernel (BLPTK), which identifies local branching and merging within policy trajectories by analyzing forward and backward conditional path distributions. The method integrates local path kernels, spectral clustering, and explicit mass-and-conductance checks to produce empirical path partitions that satisfy specific resolution criteria. The authors validate the detection capability using synthetic graphs, the D3IL-Avoid benchmark, and a simulated 7-DoF robotic arm, further demonstrating that the identified partitions can serve as branch-mass constraints during reinforcement learning (RL) fine-tuning.

Critical strengths
  1. Endpoint distributions cannot distinguish between a single path and multiple paths that diverge and subsequently reconverge. By utilizing local path-segment distributions, this paper addresses this loss of information and is supported by a clear theoretical motivation.

  2. Rather than relying solely on spectral eigenvalues to determine the number of branches, the algorithm evaluates the probability mass and conductance of each block in a proposed partition. This ensures that the output corresponds to explicit empirical feasibility criteria, rather than mere clustering results.

Critical weaknesses
  1. Low conductance is not equivalent to a genuine decision-making branch. Equation (6) defines the maximum number of path groups satisfying the mass and conductance thresholds at a chosen resolution, not necessarily the number of distinct policy decisions. For instance, different execution speeds along the same geometric route could produce separate path clusters when using time-indexed path features. Since mass and conductance checks only confirm statistical separation, they do not establish whether these clusters correspond to distinct route choices made by the policy.

  2. The branch-mass constraint can fail to penalize the loss of existing routes. Eq. (12) in Appendix C.4 assigns uniform branch membership to new paths with zero affinity to all reference paths. If the reference branches have equal weights and the current policy shifts entirely to paths with zero affinity to the reference paths, the estimated branch weights will still match the reference distribution, resulting in a KL penalty of zero. Furthermore, anchor points with low visitation rates are skipped. This implies that this regularization does not effectively constrain the preservation of the original paths.

Questions for authors

1.How can it be demonstrated that path clusters with low conductance correspond to genuine policy decision branches, rather than being statistical artifacts arising from differences in execution speed or incomplete state conditioning?

  1. When trajectories from the new policy have zero affinity to all reference paths, can the uniform fallback in Eq. (12) make the branch-mass KL penalty zero if the reference branch weights are equal? Can the authors provide an explanation of how this failure case is prevented?
1 comment
AuthorsOpenReview ↗

Response to Reviewer cEN9: what a block means (Q1) and the zero-KL fallback (Q2)

Thank you for the review. You are right on both structural points, and the revised paper says so. New results below were declared before they ran.

Q1 (also W1). How can it be demonstrated that low-conductance clusters are genuine decision branches, and not artifacts of execution speed or incomplete state conditioning?

Mass and conductance alone cannot demonstrate it, and we do not claim they can. What we propose is a formulation: local behaviour is the conditional law of a path segment given a context, in each direction, and where rollouts divide is a question posed on that law at a declared resolution. The revised paper makes this its main contribution (Figure 1), and Section 3 now states that blocks are low-conductance groups of paths, not necessarily routes. Eq. (6) is one readout of the law: it counts path groups that meet the two tests. A path group is a statement about the rollouts, and calling it a decision needs something the rollouts do not contain. In our evaluation that link comes only from an external truth: route labels on the arm and mode separation on D3IL-Avoid. Because the feature map and the context are explicit parts of the question, speed and conditioning can be tested directly, and we did so.

For execution speed, we ran the test you describe. Warping speed on the arm raises the false-positive rate of time-indexed features from 0 to about 0.02, so the mechanism is real, while arc-length features stay at 0. At native speed both are at 0, and on Avoid the choice barely matters. Arc-length's higher agreement on the arm comes from its window reaching forks at early anchors and says nothing about speed, and it means our declared test failed on the high side. The headline features stay time-indexed, with this result reported beside them.

For incomplete state conditioning, we removed parts of the context on the arm. With the full context, agreement is 0.972 and the false-positive rate is 0, against 0.670 for always-one. Replacing the obstacle-relative position with absolute position gives agreement 0.904 and a false-positive rate of 0.075, against 0.592 for always-one, so conditioning on too little does create false branches. Removing velocity changes little (0.971, false-positive rate 0). On this one task it shows what the formulation implies: the kernel is conditional on the context it is given, so an incomplete context changes the question being answered.

Q2 (also W2). Can the uniform fallback make the branch-mass KL zero when reference weights are equal, and how is this prevented?

Yes, it can, and nothing in the construction prevents it. If every current path is uncovered, the estimated masses are uniform; when the reference masses are also uniform, the KL is zero. The fallback belongs to how our penalty lifts frozen labels onto new paths, and it is not part of the kernel or the count. The revised paper separates the two: it poses route-preserving fine-tuning as reward maximisation subject to preserving local kernel masses at regions detected from base rollouts, states the gradient of such a mass, and says that our penalty is only a biased surrogate for it. We have only an empirical bound on these runs: at the selected policy, about 30% of active-anchor and rollout pairs use the fallback, and each seed's mean localisation-weighted fallback across active anchors is below 0.04%. In one monitored seed, the largest single-anchor share under the update's weights was 8.7%, at iteration 600; the largest checkpoint mean across anchors was 0.5%. This is not a batch-wide bound.

We tested two changes under the same gate. The first excludes zero-affinity paths from the mass, which tests whether the fallback carries the result; it passes 5/5 seeds, so the result does not rest on the fallback. It does not remove your case, because an anchor with no covered path is then skipped. The second gives zero-affinity paths their own block with near-zero target mass, so that moving onto them costs KL. It passes 4/5 with the same reward and routes as the original, so the outcome here does not depend on the fallback.

You are also right about low-visitation anchors. Only a little over half of the frozen anchors stay active at the selected policy, and neither change addresses that, so a policy can leave a region without paying for it. We also removed the 5% occupancy floor so that low-visit anchors enter the penalty. That passes 5/5 and keeps 59% of the reward gain, the same as with the floor, so the floor does not carry the result, but it does not close this gap either. This limit belongs to the formulation as written as well as to the penalty: the constraint is conditional on a context, so a policy that stops visiting that context has no constrained law there. Constraining occupancy too is open. The penalty does not guarantee that routes are preserved. We report that they were preserved in these runs, and we treat the penalty as a naive first instance of the formulation and not as a finished regulariser.

Reviewer_2QQiOpenReview ↗
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Paper summary

This paper introduces bidirectional local path-transition kernels for identifying split and merge structures in offline policy rollouts. The method estimates conditional distributions of forward and backward path segments, constructs affinity graphs, and validates spectral partitions using mass and conductance constraints. Its output is an empirical, resolution-dependent lower bound on local path multiplicity rather than a statistical guarantee of the underlying route graph. Experiments cover synthetic directed structures, diffusion-policy rollouts, and a simulated robotic arm. The authors also use the detected regions as constraints during reinforcement fine-tuning to preserve demonstrated route diversity.

Critical strengths

1.The proposed bidirectional path representation captures local splits and merges that endpoint-based statistics cannot reliably identify. 2.The downstream reinforcement fine-tuning experiment demonstrates the potential usefulness of detected path structures for preserving behavioral diversity.

Critical weaknesses

1.In the simulated arm experiment, BLPTK achieves 0.971 path-count agreement versus 0.961 for DBSCAN and 0.959 for agglomerative clustering using comparable path features. The paper does not establish whether this improvement translates into better downstream route preservation than clustering-derived constraints. 2.Because the reported path counts are empirical lower bounds under user-specified mass and conductance thresholds, their reliability depends on the chosen resolution. The paper does not sufficiently establish how stable these counts remain when the thresholds are selected without access to ground-truth route structure. 3.The claimed bidirectional detection capability is not fully validated, since real-policy experiments mainly examine forward splits, while merge detection relies on synthetic or time-reversed trajectories rather than independent natural merge events. 4.Although the route-preservation constraints outperform matched-dose fixed-time and fork-window KL controls, they retain only part of the unconstrained reward gain. The comparison does not isolate whether BLPTK partitions offer a better reward-diversity trade-off than simpler trajectory-clustering partitions.

Questions for authors

1.Would using DBSCAN or agglomerative clustering partitions achieve comparable route preservation under the same downstream regularization? 2.Can the proposed method identify natural merge events without relying on time-reversed trajectories? 3.How sensitive are detection accuracy and downstream performance to the path metric, affinity scale, and conductance threshold?

2 comments
AuthorsOpenReview ↗

Response to Reviewer 2QQi (1/2): clustering regions (Q1) and natural merges (Q2)

Thank you for the review. Your three questions are answered below, and they also cover W1 to W4. Each result below was declared before it ran, except where we say it is exploratory.

Q1 (also W1, W4). Would DBSCAN or agglomerative clustering partitions achieve comparable route preservation?

Yes, comparable. We let each method choose its own regions from the same rollouts, with the same penalty, dose and gate over five seeds. BLPTK and single linkage each pass 4/5. DBSCAN passes 2/5, failing only on collisions. Our declared test that BLPTK would pass more seeds than both failed, so BLPTK partitions do not give a better reward-diversity trade-off here. All three share the localisation and path features, and nearly all clustering anchors are also BLPTK anchors. We make no downstream claim for our estimator over clustering. Those clustering regions are themselves instances of what we propose: local directed path laws, read out at a declared resolution and frozen as regions. Single linkage is one readout of the empirical kernel and our acceptance test is another, and we claim the kernel's generality only for what it can express. Our contribution is the object and the formulation built on it, not a better clusterer. We also tested whether these readouts hold as rollouts grow; single linkage collapses, and ours, at the declared tolerance, does not hold either (Q3 and Appendix C.25).

Where the constraint sits matters: at the same dose, regions detected by BLPTK or by single linkage pass 4/5, while fixed-time regions and a KL penalty on the fork window pass 0/5. An unlocalised trajectory-entropy bonus passes 4/5 at its working dose, and with a 3200-iteration minimum and the same stopping rule it and our constraint both pass 5/5, entropy holding the routes more evenly and ours keeping more reward. What the local formulation adds is a statement of where the rollouts divide, which a global bonus does not provide. Re-freezing BLPTK from fresh rollouts also lowered its route diversity, so the committed result sits on the favourable side of sampling variation. The revised paper reports both.

Q2 (also W3). Can the method identify natural merges without time-reversed trajectories?

On simulated policy rollouts, yes. On the arm, where routes rejoin past the obstacle, un-reversed K-minus scores 0.945 against 0.590 for an oracle time lookup. We have no such evidence on external learned-policy data, and we concede that part of W3: D3IL-Avoid has almost no merges to detect, and its reversed run is only a code-path check. We did not find publicly available rollouts of a learned policy with natural merges.

On real driving, we ran un-reversed K-minus on openDD roundabouts, with truth from the published lane graph. On four roundabouts opened only after we repaired a fault in that truth, it has recall 0.26 to 0.63 and false alarms at most 0.03 at the declared settings, and the gate passes in both directions on two. These are human drivers, not a learned policy, and the truth repair came after a first scoring on other roundabouts, as the revised paper states.

We therefore ran un-reversed K-minus on OGBench antmaze-large-navigate, a scripted noisy expert in simulation, so this shows detection on merging paths and not on learned policies. Our first declared truth, a corridor count from the maze map, failed: agreement 0.844 against 0.869 for always-one. It treats corners as choice-free, yet 20% of corner visits turn back. Our declared test that removed turn-backs did not eliminate the excess firing at corners; the filter missed some reversals, so that explanation is incomplete. Several exploratory map-truth definitions and a withdrawn tuning attempt also preceded what follows. We replaced the truth with blind ratings of 60 panels by one author, who is not independent. On 400 episodes not used for tuning, at the declared settings, 27 of 30 fired panels were rated correct, with recall 0.39 and false alarms 0.04 when weighted back to the population, so the declared gate fails on recall. Settings tuned on 58 other rated panels pass, with recall 0.72 and false alarms 0.14, but they fail if the rater's uncertain panels count as yes. The panels were drawn for an arc-8 window and the same ratings score the arc-12 detector. Single linkage at the same window, untuned, has recall 0.49 and false alarms 0.01.

AuthorsOpenReview ↗

Response to Reviewer 2QQi (2/2): sensitivity to metric, scale and tolerance (Q3)

Q3 (also W2). How sensitive are detection and downstream performance to the path metric, affinity scale and conductance threshold?

We do not offer a detector to plug in blindly. The settings define the question being asked, and the revised paper adds a guide to choosing them. The count is one readout of a conditional path law. We use it to mark regions where local behaviour is multimodal, and a naive constraint on those regions keeps both routes on one arm task. We propose this pairing as a way to pose fine-tuning: the revised paper writes it as a constrained problem on the kernels and gives the gradient of a local mass. We do not show that it beats other ways of preserving routes, and an unlocalised entropy bonus also works here.

Detection depends strongly on the path metric: replacing the path with its endpoint costs about 0.18 of agreement on the arm. It holds near 0.97 at small scales and falls to 0.74 at the largest we tried. Run blind, our label-free rule picks ell two grid steps from our declared value, so our declared test of recovering ell failed, though agreement barely changes. It selects ell only; alpha and delta_cut stay declared. The conductance threshold matters on some toy geometries, where it does 0.88 to 0.93 of the rejecting in some cells, and hardly at all on the arm, where 87.5% of lifted partitions have exactly zero conductance and only 3.7% exceed delta_cut. Restricting the frozen anchors to delta_cut 0.005 passes 4/5 downstream, the same as the full set. A new test, declared before it ran, shows that delta_cut matters on the arm once rollouts are plentiful. The cloned policies leave both routes in 9 to 15% of rollouts, and these strays run between the routes. We grew the rollouts sixteenfold with every setting fixed at the smallest size. At delta_cut 0.005, BLPTK's agreement fell from 0.75 to 0.39, failing our declared stability gate: as the strays filled the gap, the escape probability of the true route split rose past 0.005. At 0.05, a value we chose after seeing this, detection held near 0.9, but false alarms rose to 0.22 to 0.32, above our gate. So delta_cut trades routes merged by strays against single streams split in two, which is what the tuned roundabout setting showed at 0.5. Single linkage has no such setting, and its detection fell from 0.61 to 0.04. The revised paper reports this test, with its failed gate, in Appendix C.25, and its new Limitations paragraph (Section 9) states the resolution dependence plainly.

Downstream, the dose window is narrow: 4/5 at our dose and 1/5 at a third of it or at three times it. Freezing the regions at ell 1.18 and 2.18 passes 5/5 and 4/5, against 4/5 at our declared 1.64 on the same rollouts. We have not run downstream sensitivity to the path metric.

The revised paper adds a practical guide to choosing these settings, and reports what tuning them against truth achieved on AntMaze and on roundabouts of human drivers. On the roundabouts we found a fault in our own map truth after the first scoring, which we repaired without using the detector and report openly. We then scored four roundabouts, none opened before, once each. At the declared label-free settings false alarms are at most 0.03, recall is 0.26 to 0.69, and the gate passes in both directions on two of the four. Tuned settings raise recall but mostly fail on false alarms. Tuned single linkage passes in both directions on two and in one direction on a third. Against one non-independent author's blind count ratings on 64 new panels from the four roundabouts, pooled recall is 0.69 and false alarms 0.09. A second rater, who knows the authors and was told one extra rule (two lanes on one road count as one place), rated the same panels blind. The two agree on 60 of 64 (Cohen's kappa 0.86), and the gate passes again, with recall 0.61 and false alarms 0.11 pooled; for merges alone the false alarms are 0.198, just under the 0.2 limit. Both ratings are reported in Appendix C.22. This does not validate the detector's division into routes. A later AI-assisted check on one roundabout, also not independent, with the map truth hidden during labelling, kept 10 merge false alarms, and inspection showed eight of them dividing shared road streams. We therefore do not attribute the tuned merge failures mainly to truth errors.

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

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