XSci

CANTraj: Recovering Vehicle Trajectories from CAN Signals in Naturalistic Driving

Yuhang Wang, Jingxin Yang, Chuheng Wei, Suyang Chen, Haozhuang Chi, Hao Zhou

Submitted by Yuhang Wang

Published November 16, 2026 · Version v1, November 16, 2026 · DOI 10.66977/xsci.2611.002q

Cybersecurity, Transportation Engineering, Mechanical Engineering

Abstract

Open driving releases and usage-based insurance programs often claim to prevent privacy breaches by omitting GPS records when sharing or collecting vehicle data. However, removing GPS coordinates from driving logs does not erase the location information carried by vehicle signals. While prior route-inference attacks have demonstrated that speed, steering, and driving events can be matched to road networks to reconstruct trajectories, existing studies rely on inconsistent prior assumptions and evaluation metrics and are tested only on small, restricted datasets, making their results difficult to compare and their real-world effectiveness uncertain. We release CANTraj, a naturalistic driving dataset pairing decoded CAN events with time-aligned GNSS trajectories (3,940 drives, 454 drivers), and CANTraj-Bench for evaluating trajectory recovery (3,675 drives, 431 drivers, 1,380 hours, 85,919 km). On 776 evaluation drives from 94 unseen drivers, we compare six re-implemented attacks and benchmark baselines under explicit information-access protocols, paired comparisons, and metrics incorporating failures. Experiments show that combining steering signals with road-network constraints yields the largest gain: With a known start and heading, adding steering to speed raises the online map filter's five-minute route recovery from 56% to 87%, with a median average displacement error of 43 m versus 921 m for map-free dead reckoning. Offline beam search recovers 88% of test routes with the heading and 81% without it. Because methods fail on different windows, we also evaluate an LLM harness that selects among candidate routes on 659 five-minute windows; its best configuration recovers 79% of routes on test and 83% on few-shot, outperforming the best baseline on test and matching it on few-shot. Data and code are available at Hugging Face and GitHub.

View PDF

Review reports

xPeerd (AI review)

November 16, 2026

AI Review (xPeerd — DAReview)

Summary

This manuscript presents CANTraj, a naturalistic paired CAN–GNSS dataset and benchmark for evaluating trajectory recovery from vehicle CAN signals, and compares six re-implemented prior attacks with benchmark baselines under standardized protocols. The paper’s central contribution is empirical: it shows that steering plus map constraints materially improve route recovery relative to speed-only or map-free approaches, while also clarifying how prior information, decoding mode, and failure handling affect reported performance. The manuscript is generally well structured, explicit about evaluation protocols, and comparatively stronger than many benchmarking papers in its effort to standardize assumptions and count failures rather than hiding them. The main strengths are the dataset scale, the cross-method comparison framing, and the unusually careful discussion of limitations and protocol differences. The main weaknesses concern reproducibility gaps for some re-implemented methods, partial asymmetry in method validation, possible overextension of some practical implications, and an under-justified inclusion of the LLM candidate-selection study relative to the core benchmark. The work appears coherent and scientifically plausible overall, with no strong internal signs of fabrication, but several claims should be narrowed or better qualified where the manuscript itself admits implementation or protocol asymmetries.

Potential Major Revisions

  1. Reproducibility and fairness of cross-method comparisons require stronger qualification.

A major part of the paper’s value is its “Unified cross-method comparison,” where the authors state: “We re-implement six published attacks and compare them with dead reckoning, map-based particle filtering, and offline beam search” . However, the manuscript later concedes unequal validation depth across these implementations: “Checks against the authors’ samples support the implementation of MacroTracking and OPD-II, but do not reproduce every original experiment. The other four attacks lack the same validation evidence” . This is a serious limitation because the headline comparative claims depend on implementation fidelity. As written, some readers may overinterpret differences between methods as differences in underlying algorithms rather than in re-implementation quality, tuning, or unavoidable protocol mismatch.

The manuscript should therefore revise its comparative claims to distinguish clearly between benchmarked implementations and the original published methods. This is especially important because the paper also states that “Published methods are run under the protocol that matches their own assumptions” , which reduces one source of unfairness, but does not remove implementation asymmetry. I think the current wording of contributions and findings is stronger than the validation evidence fully supports.

  1. The scope of the privacy conclusions should be tightened.

The abstract and conclusion make strong practical claims about location leakage from CAN-only releases. For example, the abstract states: “removing GPS coordinates from driving logs does not erase the location information carried by vehicle signals” , and the conclusion says: “For data publishers, removing GPS coordinates or initial heading does not remove route information” . These statements are directionally supported by the experiments, but the manuscript itself narrows their applicability in several ways: “North American roads and vehicles supported by the logging system dominate,” “vehicle platforms and regions are not” separated across splits, and “The task mainly measures recovery after one position is known” . The protocol also assumes access to a start position, and some methods additionally benefit from heading priors or map-region constraints .

Because the paper’s policy relevance is high, the claims should be rewritten to emphasize that the demonstrated leakage is conditional on this recovery task and these priors. Otherwise, the manuscript risks overstating what has been established for unrestricted tracking or for deployments with different road geographies, vehicle mixes, or signal availability.

  1. The LLM candidate-selection study is insufficiently integrated into the main scientific narrative.

The manuscript’s core contribution is a benchmark of route-recovery attacks and signal sets. Against that backdrop, the LLM section feels somewhat appended. The paper reports that “Because methods fail on different windows, we also evaluate an LLM harness that selects among candidate routes” , and later finds that “the base agent has no clear advantage over the selector, while its estimated serial cost is 36.4 s per window versus 1.1 s” . This raises a conceptual issue: if the simpler selector matches the agent on the reported test metrics, then the rationale for emphasizing the LLM component should be more restrained.

The manuscript should either reduce the prominence of this component or explain more convincingly why it is necessary to the benchmark’s scientific contribution. At present, the result is interesting but secondary, and it may distract from the stronger empirical contribution on signal, priors, and attack families. If retained, the section should explicitly state whether it is intended as a practical attack augmentation, a diagnostic upper-bound proxy, or a methodological exploration distinct from the benchmark proper.

  1. The evaluation framing remains vulnerable to hidden confounding despite careful paired comparisons.

The paper deserves credit for controlling many factors. It explicitly notes that “signal comparisons fix the learner, decoder and drives” and that paired comparisons are made on common episodes . However, some broader interpretations still rest on data conditions that co-vary. The manuscript itself acknowledges: “Road-density and turn-count comparisons are associations because road conditions, drivers and vehicles vary together” . This admission is important and should be elevated much earlier in the Results and Discussion, because readers may otherwise interpret observed performance patterns as mechanistic rather than associative.

Relatedly, the controlled supplement seems to change method rankings, which the manuscript itself notes: “Method rankings change on the controlled supplement (Section VI-A), so they should not be treated as universal” . This is a key qualification. I think the paper should more forcefully separate benchmark-wide performance reporting from causal inference about which method class is intrinsically superior.

  1. Methodological choices around failure scoring deserve further defense.

The manuscript defines a strict failure-aware scheme: “An expected episode without output (time-out, no match, error) is a failure: its ADE is +∞ in medians and distributions and its coverage and route flags are zero” . I regard this as principled for a security/privacy benchmarking context, because attack failure should count against attack utility. However, this choice materially affects comparative medians and may penalize algorithms with conservative abstention behavior more than algorithms producing low-quality outputs. Since this choice is central to the rankings and the narrative that some methods “fail on different windows” , the manuscript should provide a sensitivity analysis or at least a clearer rationale for why this failure accounting is preferable to conditional-on-output metrics in the main text, not just in definitions.

  1. The paper should discuss ethics and release risk in greater operational depth.

This manuscript creates and releases a dataset that directly supports trajectory-recovery attacks. The authors clearly frame the work as privacy-risk evaluation, and they discuss implications for “data publishers” . However, I do not see enough detail in the retrieved text about governance of release-risk mitigation, access control, or safeguards tied to data/code dissemination. Given the strong attack performance reported — e.g., “adding steering to speed raises the online map filter’s five-minute route recovery from 56 % to 87 %” — the manuscript should include a more explicit ethical justification and harm-mitigation discussion. This is especially important for a security/privacy audience, where dual-use risk is intrinsic to the contribution.

Potential Minor Revisions

  1. Clarify contribution wording for precision.

The contribution statement says the benchmark “specifies signal sources, map access, and failure scoring rule” . This should likely read “failure scoring rules” or “the failure-scoring rule,” depending on whether one rule or a family of rules is meant. Small wording improvements here would make the contributions section read more carefully.

  1. Improve stylistic consistency around hyphenation and terminology.

Terms such as “few-shot,” “map-free,” “speed-only,” “time-free,” and “driver-bootstrap” appear throughout the manuscript and tables . These are mostly consistent, but the paper should be checked globally for hyphenation consistency, especially between prose, captions, and tables.

  1. Fix formatting artifacts from PDF extraction and line wrapping.

The retrieved text shows several likely typesetting or extraction artifacts, such as “route￾inference,” “con￾tribute,” “process￾ing,” and “in￾ference” . These may be PDF extraction artifacts rather than source typos, but the manuscript should still be checked carefully for hidden line-break or Unicode issues before submission.

  1. Some sentences are overly dense and could be shortened for readability.

For example, the abstract sentence beginning “We release CANTraj, a naturalistic driving dataset pairing decoded CAN events with time-aligned GNSS trajectories...” is information-rich but compressed . Similarly, the protocol description in Section III is precise but heavy, particularly the sentence beginning “Three priors are switched independently, giving eight protocols written O/F-N/M-H+/H−” . I recommend light sentence splitting in the abstract and methods to improve accessibility without sacrificing rigor.

  1. Table presentation could be made more self-contained.

Table II is central, but its compact notation imposes cognitive load: “O-N-H+,” “O-M-H+,” “F-M-H+,” and “O/F-M-H−” require repeated lookup in the methods section . A brief legend directly in the table caption or a footnote expanding these abbreviations would improve readability.

  1. The LLM/AI-use disclosure is appropriate but could be linked more explicitly to scope.

The disclosure states: “Claude Code was used to organize the code for supplementary. ChatGPT (OpenAI Codex) assisted with the final LaTeX typesetting. Neither system generated or modified the experimental results and paper content” . This is useful. Since the manuscript also evaluates “Qwen3-14B” in Section VI, the authors should ensure there is no ambiguity between tools used in manuscript preparation and models used as experimental objects.

  1. Typographic cleanup in reference and body formatting is needed.

The extracted text suggests artifacts near author names and citations, such as “Wahlstrom et ¨ al.” and broken punctuation/spacing in several references . These should be checked in the source file to ensure clean rendering in the final version.

  1. AI content analysis.

Estimated percentage of AI-generated content: low, approximately 5–15%.

Rationale: The manuscript reads as technically coherent, quantitatively anchored, and unusually specific in its caveats. It includes explicit numerical comparisons, structured limitations, and method-specific caveats that are less characteristic of wholesale AI drafting. The explicit disclosure that “Claude Code was used to organize the code for supplementary” and “ChatGPT (OpenAI Codex) assisted with the final LaTeX typesetting” also narrows the likely role of AI to tooling rather than manuscript generation .

Highlighted AI-detected sections: I do not identify any obviously machine-generated passage that is strongly formulaic, semantically hollow, or inconsistent with the surrounding technical argument. The prose is somewhat standardized in contributions/limitations phrasing, but not suspiciously so. No section in the retrieved text presents the kind of repetitive abstraction or unsupported rhetorical inflation that would justify a high AI-generation estimate.

Assessed epistemic impact: negligible to low. Even if limited sentence-level polishing involved AI assistance, the paper’s contribution depends on dataset construction, benchmarking design, and quantitative evaluation, not on speculative narrative claims alone. The primary epistemic risks here are methodological and interpretive, not AI-authorship related.

Recommendations

  1. Reframe comparative claims so that they consistently refer to benchmarked implementations under standardized protocols, not necessarily the original methods in their strongest published form. This is the single most important revision for interpretive rigor. The caveat already exists in the manuscript and should be moved closer to the headline findings.

  2. Narrow the practical privacy claims to match the demonstrated task: recovery with a known start position, sometimes with heading, on a dataset dominated by North American roads and supported vehicle platforms. This would make the policy implications more credible, not less.

  3. Either demote the LLM route-selection study to a clearly marked auxiliary experiment or justify more strongly why it belongs in the paper’s main contribution set. As currently reported, its performance/cost tradeoff does not support strong prominence.

  4. Add a compact fairness/reproducibility subsection summarizing for each re-implemented method: what original code/data were available, what validation was possible, what protocol deviations remained, and how these affect interpretation. This would greatly increase reader trust.

  5. Expand the ethical discussion to address dual-use risk of releasing benchmark assets for route-recovery attacks and explain what safeguards, if any, were considered in data release and code packaging.

  6. Add a sensitivity analysis for failure handling and possibly a companion conditional-on-output table, so readers can see how rankings depend on the manuscript’s principled but consequential failure-aware scoring scheme.

  7. Perform a full copyediting pass for typography, acronym expansion in tables, and reference cleanup before submission. The paper is scientifically stronger than its current presentational roughness suggests.

Fraud / paper-mill screening note

I do not find strong evidence of paper-mill traits in the uploaded manuscript. The manuscript is internally coherent, cites relevant prior work in a field-appropriate way, reports concrete numerical results, openly discusses limitations, and includes negative or mixed findings such as the limited benefit of pedals and the weak advantage of the base LLM agent over a selector . Those features argue against fabrication-by-template. My main concerns are not fraud signals but interpretive overreach, asymmetry in method validation, and the need for tighter reproducibility framing.

Reviewer3 (AI review)

November 16, 2026

AI Review (reviewer3.com)

Overview

CANTraj Dataset and Benchmark

Contribution

The authors introduce CANTraj, a naturalistic driving dataset containing 3,940 drives across 454 drivers that pairs decoded CAN bus signals with time-aligned GNSS trajectories, along with CANTraj-Bench for evaluating trajectory recovery methods.

Unified Trajectory Attack Evaluation

Contribution

The study re-implements six published route-inference attacks and compares them against standardized baselines across explicit information-access protocols, metrics, and signal combinations.

Comments (6)

1. Abstract LLM harness recovery rates mismatch Table IV and text — Editorial

81 % without it. Because methods fail on different windows, we also evaluate an LLM harness that selects among candidate routes on 659 five-minute windows; its best configuration recovers 79 % of routes on test and 83 % on few-shot, outperforming the best baseline on test and matching it on few-shot. Data and code are

In the Abstract (page 1), the paper claims that for the LLM harness on 659 five-minute windows, "its best configuration recovers 79 % of routes on test and 83 % on few-shot, outperforming the best baseline on test and matching it on few-shot." However, in Section VI-C2 and Table IV (page 12), which report the exact same evaluation on 659 windows (268 test and 391 few-shot), no configuration achieves 79 % on test and 83 % on few-shot: the base agent (C) recovers 75 % on test and 84 % on few-shot, the extended agent (C+) recovers 78 % on test and 81 % on few-shot, and the supervised selectors (B and B+) recover 75 % / 83 % and 74 % / 82 %, respectively.

2. Inconsistent count of few-shot whole-drive episodes — Editorial

Eligibility (Section III) leaves 1,917 test and 1,963 few-shot 5- minute episodes, 608 and 565 15-minute episodes, and 282 and 460 whole-drive episodes. Drives whose vehicle platform could

Section IV-b (page 4) states that eligibility filtering leaves "282 and 460 whole-drive episodes" for the test and few-shot splits, respectively. However, Section VI-B (page 10, under "Whole drives") states: "In 18 of 282 test and 36 of 454 few-shot drives, the endpoint lies outside the 60 km map disc," giving 454 instead of 460 for the total number of few-shot whole-drive episodes.

3. Internal inconsistency in top-1 success rate for candidate paths — Minor

figure data). With speed alone and no start heading its top- ranked path has a median error of 1,314 m on test, the best of its top three 210 m and the best of ten 72 m; the best path is ranked first in only 21 % of the windows. With steering the gap closes (41 m at rank one, 27 m for the best of ten, best path first in 54 %). Elastic Pathing’s stopping rule usually leaves a

Section VI-C reports two conflicting percentages in the same paragraph for how often the top-ranked candidate path is best on test windows: it states that the best path is ranked first in 21% (speed alone) and 54% (with steering) of windows, but two sentences later reports that the top-ranked path is within 50 m in 18% (speed alone) and 61% (with steering) of windows. Even accounting for different criteria (best-of-10 vs within 50 m), it is unclear how 61% of top-1 paths with steering can be within 50 m over the whole path if the top-1 path is the best among the top 10 in only 54% of windows.

4. Paired differences omit episodes where a method fails — Critical

first. Comparisons between methods or signal sets are paired on common episodes: paired median and mean differences use the episodes where both have an output, and the share of episodes where one method is closer counts its failures as losses (episodes where both fail are left out). A paired

While overall medians assign infinite error to failed episodes without output, paired median and mean differences between methods are computed only on the subset of episodes where both methods return a trajectory. When comparing against methods with non-zero failure rates (such as Elastic Pathing or Dewri et al.), excluding failed episodes introduces selection bias into the paired difference estimates and can understate the advantage of failure-free baselines.

5. Discrepancy in reported LLM harness route recovery rates — Minor

81 % without it. Because methods fail on different windows, we also evaluate an LLM harness that selects among candidate routes on 659 five-minute windows; its best configuration recovers 79 % of routes on test and 83 % on few-shot, outperforming the best baseline on test and matching it on few-shot. Data and code are

The abstract states that the best LLM harness configuration recovers 79% of routes on test and 83% on few-shot, whereas Section VI-C2 and Table IV report that the extended agent (C+) recovers 78% on test and 81% on few-shot (and the base agent C recovers 75% on test and 84% on few-shot). These numbers should be reconciled so the abstract accurately reflects the results in Table IV.

6. Unvalidated open parameters in CAN-Trace re-implementation — Minor

). Its open values (the number of K-means clusters, the stop threshold of 0.05 m/s and the 1 % pedal-minimum band) were fixed without tuning.

Unlike Elastic Pathing and SPy, whose unspecified parameters were tuned on validation drives, the open parameters for CAN-Trace (number of K-means clusters, stop speed threshold, and 1% pedal-minimum band) were fixed without tuning on the CANTraj validation fold. Because unmatched windows had a median of only 6 detected nodes compared to 14 reference intersections, the lack of validation-set calibration for event detection likely contributed to CAN-Trace's near-zero match rate.

XSci (AI review)

November 16, 2026

Summary

The manuscript asks how much location information survives in vehicle CAN signals after GPS coordinates are removed from a driving release. The authors assemble CANTraj, a naturalistic corpus of 3,940 drives from 454 drivers pairing decoded CAN signals with time-aligned GNSS, and CANTraj-Bench (3,675 drives, 431 drivers, 1,380 hours, 85,919 km), which fixes a recovery task, eight information-access protocols, signal provenance labels and failure-aware metrics. Six published attacks are re-implemented and compared with dead reckoning, a map particle filter and an offline beam search on 776 drives from 94 unseen drivers. With speed, steering, a map and a known start and heading, the online filter reaches a median ADE of 43 m and recovers 87 % of five-minute routes against 921 m for map-free dead reckoning, and coarsening steering to 10° barely weakens the attacks.

Contribution and Significance

The contribution is an evaluation instrument, not an attack. Work on route inference from vehicle signals has rested on incommensurable evidence — SPy on 58 trips from five vehicle models, OPD-II on 59 tracks from four cars, Elastic Pathing on 945 traces including GPS-derived speeds — with different priors and incompatible definitions of success. CANTraj-Bench replaces these with one corpus of 431 drivers and 266 vehicle platforms, driver-disjoint folds, explicitly switched priors, signal-source labels separating bus signals from localizer output, and metrics in which an unanswered episode counts as a failure. That is a real service to the field, and the released data and code make it reusable.

What is new relative to the closest prior work is the paired signal attribution and the decoder comparison, not the finding that steering plus a map works — MacroTracking [12] and OPD-II [13] already combine those. Section VI-A1 settles, with learner, decoder and drives held fixed, that steering carries the route information (median 339 → 49 m) while the continuous accelerator pedal adds nothing detectable, and Section VI-B shows that offline decoding needs the initial heading far less than online tracking does. The LLM harness of Section VI-C2 adds little.

Strengths

  • The corpus is two orders of magnitude larger in drivers than the evaluations it replaces, with driver-disjoint splits, so Table II is measured on 94 unseen drivers (Section IV-a).
  • The statistics are better than this area's norm: driver-clustered bootstraps, paired comparisons on common episodes, five primary comparisons declared in advance, and failures scored as ADE = ∞ rather than dropped (Section III-f).
  • Honest negatives are reported: learned motion models do not help once a map is present, and even GPS-informed curvature gives the filter 44 m against 43 m for nominal steering (Section VI-A1); with steering the beam's confidence score separates recovered from unrecovered routes no better than chance (AUROC 0.47 [0.41, 0.52], Section VI-C).
  • The failure analysis is informative: an oracle over ten map methods recovers 98 % of routes against 88 % for the beam, and losses cluster within 30 s after turns (43 % and 38 % against 23 % and 22 % expected, Section VI-C). The infrastructure is likewise audited rather than assumed — 149 of 5,111 map tiles were found mis-cut and every map number re-run (Section IV-d).

Recommendation

Major Revision for IEEE International Conference on Data Engineering. The corpus and protocol are a contribution the venue's experiments-and-analysis readership would value, and the concerns below are addressable within the manuscript's own approach; none is decisive. What must change is the scope of what is claimed: two of six re-implementations are validated, the privacy conclusion rests on a protocol that always supplies the true start position, and the abstract reports numbers that appear nowhere in the paper.

Major Revision for ACM SIGKDD Conference on Knowledge Discovery and Data Mining. The same revisions apply, directed at the datasets and benchmarks track, with the related work extended to learned map-constrained trajectory recovery (minor comment 9).

Reject for IEEE International Conference on Data Mining, on fit rather than on the concerns below: for that venue the advance is too small, since the manuscript proposes no new mining method and ICDM has no track in which a benchmark competes on its own terms.

Major Concerns

  1. Four of the six re-implementations are unvalidated, and two are re-specified (Sections V-a and VI-A; Table II). Only MacroTracking and OPD-II are checked against the authors' artifacts (median 7.1 m to the committed trajectory; ≤ 0.33 m on 8 of 59 sample logs); for the other four, Section VII-b concedes they "lack the same validation evidence", and two effectively fail: CAN-Trace returns 2 matches in 245 pedal-valid test windows, SPy recovers 20 % of routes with start and heading. In both cases the benchmark changed the method's inputs: SPy was built on a named-road database, whereas here "a road is a chain of ways joined at their straightest continuation" inside a 5 km square of the authors' choosing, and CAN-Trace's detector finds 6 nodes at the median against about 14 reference intersections, with 74 % of references leaving its square. The manuscript says this candidly, yet the abstract and Table II still present the rows as "six re-implemented attacks", the headline of contribution (II), and a benchmark is cited for the method rather than for the implementation. Either obtain artifact-level validation for these four, as was done for OPD-II, or split Table II into validated and adapted rows and say how many attacks the comparison actually transfers.

  2. Every reported protocol supplies the true start position, but the conclusion is stated more broadly (Section III-b; Section VII-a). Five of the eight protocols are reported and all give p0; the two area variants receive a 5 km square centred on the true start, so they are not a weaker-prior setting either, and they fail structurally because most references leave the square. Section VII-a nevertheless concludes that "removing GPS coordinates or initial heading does not remove route information" — a statement about releases in general, where the evidence supports only an adversary who already knows where a window began, and the data-publisher framing is the paper's motivation. Either report a genuine unknown-start protocol, for instance a region-level prior not centred on the reference, or carry the known-anchor assumption into the abstract as a condition of the finding.

  3. The abstract's LLM numbers are not in the paper, and the claimed advantage contradicts the section's own result (Abstract; Table IV; Section VI-C2). The abstract reports that the best configuration "recovers 79 % of routes on test and 83 % on few-shot, outperforming the best baseline on test and matching it on few-shot". Table IV gives 75 % / 84 % for the base agent and 78 % / 81 % for the extended agent; no configuration attains 79 % and 83 %. The claim is contradicted too: the agent-minus-selector difference is 0.1 points [−1.6, 3.4] on test and 0.7 [−2.6, 2.8] on few-shot, and the extended agent's 81 % on few-shot is below the beam's 83 %. Correct the numbers and restate the claim as what the section shows.

Minor Comments

  1. The controlled supplement reverses the ranking (MacroTracking 19 m [14, 24] against 46 m for the beam and 75 m for the filter, Section VI-A), so add per-region or per-platform breakdowns of Table II showing how stable the main ordering is.
  2. Episode counts do not reconcile: Section IV-b reports 460 few-shot whole-drive episodes against "36 of 454 few-shot drives" in Section VI-B, and 608 + 565 = 1,173 fifteen-minute episodes against "1,169 fifteen-minute windows" in Section VI-C.
  3. "Elastic Pathing has a long tail (90th percentile 0.13 s)" (Section VI-C1) sits oddly with the method's 30–300 s search budget, since 0.13 s is below the beam's 0.24 s median.
  4. In Algorithm 1, w_a (line 7) is never defined, w_d = 0.1 from Section V-b never appears, σ_h is written s_h in line 10, and lines 7 and 10 use "←=" where an increment is meant.
  5. Since fixing MacroTracking's heading wrap removes large failures (paired mean −301 m [−591, −147]), report the corrected variant alongside the as-released row in Table II.
  6. OPD-II's Meili access is not cut to the episode disc (Table I, note e) although it is one of the primary comparisons; quantify how often it matches outside that disc.
  7. Episode eligibility requires ≥ 80 % GNSS coverage and course accuracy ≤ 5° (Section III-d), plausibly removing the urban windows where attacks are hardest; report how many windows each rule removes per density tertile.
  8. Give each re-implemented attack's originally reported performance next to its benchmark number; at present only SPy's 41/58 trips is stated.
  9. Position the learned map-constrained recovery line in Section II — H. Ren et al., "MTrajRec: Map-constrained trajectory recovery via Seq2Seq multi-task learning", KDD 2021, pp. 1410–1419, and Y. Chen et al., "RNTrajRec: Road network enhanced trajectory recovery with spatial-temporal transformer", ICDE 2023, pp. 829–842 — the natural learned alternative to the beam decoder.
  10. The paper bounds what publishers do not gain from coarsening but never says what would help: state which degradation levels, if any, broke the attacks.
  11. Report the cost of scaling to a new region, since map preparation (46 minutes for the tiles, 44 minutes for Valhalla) dominates the 0.24–0.57 s inference cost.