1.The central contribution is insufficiently substantial.
The principal result is that local search produces considerably better tours than fixed-start nearest-neighbor construction. The paper itself acknowledges that strong baselines and transparent evaluation are established principles (§1). Demonstrating this separation across four small settings provides limited new insight into neural combinatorial optimization. The manuscript does not identify a concrete conclusion from existing neural-TSP evaluations that changes under its controls, or provide an explanatory analysis of the observed neural/classical differences. The novelty and significance relative to the evaluation literature discussed in §2 remain inadequately established.
2.The experimental scope is too restricted.
All experiments concern two-dimensional Euclidean TSP with only 20 or 50 nodes and two synthetic generators. There are no larger instances, established external benchmark datasets, or additional routing problems. Separately training models for every size/distribution combination also provides no evidence about transfer. A TSP-focused study can be valuable, but the combination of small problem sizes, limited distributional coverage, and shallow analysis substantially limits the significance of this particular study. The number of held-out instances does not compensate for the narrow range of settings.
3.The learned baselines are insufficiently validated, and lack advanced neural solver baselines.
The local AM and POMO configurations are explicitly not exact reproductions of the original training recipes. In particular, AM has approximately 21.62% and 30.48% gaps on uniform and clustered TSP50, respectively (Table 2). These results warrant a careful investigation of training adequacy and implementation choices. The manuscript provides neither learning curves nor comparisons with verified reference checkpoints, and Appendix A omits important architecture and optimizer settings. Consequently, the neural/classical ordering is difficult to interpret beyond the particular trained models. The reported results do not establish whether the observed gaps reflect adequately trained baselines.
4.The comparisons do not establish practical competitiveness.
AM uses single-start decoding, POMO uses 20 or 50 starts, and the classical methods operate under different search budgets (§§4–5). No measured runtimes or solution-quality-versus-time curves are provided. Although these differences are acknowledged, the experiments cannot determine performance at comparable computational cost. The classical comparator set is also limited to NN and relatively simple local-search controls; a stronger heuristic such as the cited Lin–Kernighan implementation would make the evaluation more informative. The initialization of 2-opt and sampled 3-opt should also be specified explicitly.
5.The available artifacts do not support the emphasis on auditability.
Section 10 states that the release excludes checkpoints, raw per-instance data, logs, and environments, with some artifacts only planned for future release. Hashes and manifests record provenance but cannot substitute for the underlying materials needed to verify the results. This is a consequential limitation for a paper whose contribution relies heavily on controlled, independently auditable evaluation.
6.The presentation is repetitive and poorly prioritized.
The same gap ranges, checkpoint-selection procedure, and qualifications about scaling and method-family rankings recur throughout the abstract, introduction, results, discussion, and conclusion. Meanwhile, the comprehensive four-block results table appears only in Appendix C. The manuscript devotes considerable space to repeated procedural statements while giving insufficient attention to the unresolved scientific question and the interpretation of the findings. Consolidating these statements and bringing the central results into the main text would improve clarity, but substantial additional analysis would still be needed.