acceptodds
Under review as a conference paper at ICLR 2027

Multi-Agent Route Construction for Routing Foundation Models

Abstract

Routing foundation models pretrain one policy across vehicle routing variants and transfer it when constraints, fleets or objectives change. We develop a multi-agent interface organized around vehicle and partial-route states and route–customer extensions. Allocation-driven rollouts diversify pretraining of separate source backbones on 16 CVRP variants, and configuration comparisons link multi-depot transfer to route-slot tokens and a geometric prior. We evaluate weight-frozen transfer under supplied constraint features and feasibility masks, and fine-tuning with new vehicle attributes and objectives. Frozen reuse gives in-distribution costs comparable to the strongest baseline, a 17.19% mean gap on 32 unseen variants at against 34.89% for that baseline with the lowest gap on 28 of them, and the lowest neural gap on 37/65 CVRPLib instances. At 1M fine-tuning samples, our adaptation pipeline has lower costs than both adapted multi-task baselines in all min-max cells and in three of four min-sum cells. Within our architecture and a fixed recipe, pretrained fine-tuning at 200K target exposures reaches lower mean cost than scratch training at 1M in each of three fleet settings over three downstream seeds.

Primary area:
applications to robotics, autonomy, planning
Keywords:
neural combinatorial optimization, vehicle routing, reinforcement learning, cross-task generalization

Reviews

Among:
Shape:
1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_dxBHOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper focuses on the multi-agent workflow for routing problems. They design a geometric distance prior for the attention logits that is helpful for the decision makings of the next action. Extensive experiments also validate the power of fine-tunning stage.

Critical strengths
  1. The frozen-transfer results are promising: at N=100, the mean gap on unseen variants decreases from CCL’s 34.89% to 17.19%, with the lowest gap on 28/32 variants.

  2. The three-seed comparison provides useful evidence that pretrained initialization improves downstream performance under same training paradigm.

  3. The whole arch is easy to follow.

Critical weaknesses

The authors may miss one important reference: Wang Y, Jia Y H, Chen W N, et al. Distance-aware attention reshaping: Enhance generalization of neural solver for large-scale vehicle routing problems. This paper also proposes a very similar geometric distance prior to the neural solver. I think you should somehow compare with it in the formulation and experiments if possible.

Questions for authors
  1. Why does the N=50 full model have an unseen gap of 11.740% in Table 4 but 13.965% in Table 8, with 400 candidates in both cases? Please identify any differences in datasets, checkpoints,or evaluators.
5 comments
AuthorsOpenReview ↗

Response to Reviewer dxBH (1/2): W1, relation to DAR

We thank the reviewer for the careful review and for the two precise points. Both led to changes in the revised PDF, which are listed in the General Response.

W1. Relation to DAR (Wang et al.). Thank you for pointing us to DAR. The revised PDF cites it and adds the comparison below.

Formulation. DAR adds a distance score to the decoder compatibility of a single-vehicle POMO decoder: b = −log d for the K nearest nodes and −d otherwise (K=100, C=50). Its goal is to reduce attention dispersion when a CVRP solver trained at N=100 is applied to larger instances. Our term in Eq. (2) is the case of the same score in which K covers every scored target (with C=10): every candidate receives −log d. We therefore do not claim the distance term as a contribution, and the revised PDF states this next to Eq. (2) in §4. In our model, the distance is measured from each route slot's own current position, and the term enters a single softmax over all route–customer and route–depot pairs, both in multi-variant pretraining and in frozen transfer to unseen constraints.

Does the prior explain our gains? It helps both models but does not explain the difference between them. For instances with at most 100 customers, DAR's score is the same −log d branch as ours (the clipping constant and the decoder differ), so the controls reported for Reviewer jAXk (Q1) also measure a DAR-type prior. Mean gap (%) on the 32 unseen variants (N=50, all depots encoded):

without priorwith −log d (DAR's score, K covering every target)
RF-TE32.1421.52 (retrained)
Ours17.9911.74

The prior helps both models, which supports DAR's idea. Our model is 14.2 pp below RF-TE without the prior and 9.8 pp below with it, and our model without the prior is already below RF-TE with it.

DAR's large-instance component. DAR's −d branch acts only on instances with more than K=100 customers. On CVRPLib-X (100–1,000 customers) we replaced our term with DAR's at inference (K=100), keeping the checkpoint, the 400 candidates and the seed fixed. The mean gap rose by 0.67 pp on N ≤ 250 and by 0.30 pp on N ≥ 500, and was higher on 47 of the 65 instances (lower on 12, equal on 6). This does not evaluate DAR trained end to end with our decoder: our model was trained with −log d over all candidates, so it shows only that the inference-only swap worsens both group means. We add DAR to the related work and this comparison to Appendix C.

AuthorsOpenReview ↗

Response to Reviewer dxBH (2/2): Q1, Table 4 vs. Table 8

Q1. Table 4 (11.740%) vs. Table 8 (13.965%). Thank you for catching this. The dataset, checkpoint and candidate budget are identical; the difference comes from our evaluation script: the multi-depot (MD) slot layout (2.1 pp) and the way our gap was computed (0.1 pp).

  • Dataset. Both use the same 32 unseen variants × 1,000 test instances at N=50.
  • Checkpoint. Both use the same N=50 source checkpoint (Table 6; best validation epoch 295, Appendix B.3).
  • Candidates. Both use 8 × 50 = 400 candidates.
  • Evaluator. Our N=50 values in Table 8 were produced by an earlier version of our evaluation script that predates the MD slot layout specified in Section 4.4 and Appendix A.2. That version assigned slots to depots in contiguous blocks and clamped the active-slot count below at 1 rather than at the number of depots D. Because a rollout activates a prefix of slots, rollouts with few active slots could leave a depot without any vehicle. For example, an N=50 MD instance has D=3 depots and K=8 slots. The earlier script assigned them as (0,0,0,1,1,1,2,2), so a rollout that activates M=5 slots (e.g., c≈1.5 for an instance of average demand) uses depots 0 and 1 only, and customers near depot 2 must be served from a farther depot. Under the specified layout (0,1,2,0,1,2,0,1), every M≥3 activates all three depots. Training is unaffected, since all 16 training variants are single-depot, where both layouts coincide.
  • Gap computation. In the submitted Table 8, our gap was computed from our mean cost and the reference cost implied by the CCL row. Our N=50 gaps are now averaged per instance, as in Table 4 and the baseline columns.

To separate the two effects, we re-ran the earlier layout with the same checkpoint, candidates and evaluation seed:

Mean gap (%), N=50Earlier layout, gap as in Table 8 (submitted)Earlier layout, per-instance gapCurrent layout, per-instance gap (Table 4)
Single-depot MB (8)7.597.667.66
Multi-depot (24)16.0915.9213.10
All unseen (32)13.9713.8611.74

Re-running the earlier layout and computing the gap as in the submission gives 13.98% (Table 8: 13.97%). Averaging per-instance gaps changes this by 0.1 pp, and the slot layout accounts for the remaining 2.1 pp, all of it on MD variants. One single-depot variant, VRPMBL, differs from the submitted cost by more than seed noise (10.242 in this re-run and 10.245 in the current evaluation, vs. 10.216 submitted); we could not trace this value. Across five evaluation seeds of the current script, the standard deviation of each group mean is at most 0.01 pp. Baselines use their official environments and are unaffected.

Revision. Our N=50 column of Table 8 and the N=50 per-variant unseen table now report the current script with per-instance gaps, from the same evaluation as Table 4: 11.74% (CCL 27.59% with its published inputs, 18.73% with all depots encoded). OVRPMBTW, a near-tie in the submission (4.64% vs. CCL's 4.66%), is now 4.73%, so our gap is the lowest of the compared systems on 27/32 variants instead of 28/32, and lower than CCL's on 31/32. Both counts are the same with all depots encoded in the baselines. Tables 4 and 8 now agree on the N=50 unseen mean of the full model. We also corrected the statement that all unseen evaluations use 400 candidates; at N=100 every method uses 800 (§5, Appendix C). Appendix C now describes the earlier slot layout and gap computation.

All changes in the revised PDF are listed in the General Response. We hope this addresses the relation to DAR and the difference between Tables 4 and 8, and we are happy to answer further questions during the discussion.

Dear Reviewer dxBH

Thank you for your time and feedback. We have responded to your comments and questions and would appreciate it if you could take a look at our responses when you have a chance.

Please let us know if any concerns remain or if additional clarification would be helpful. We would be grateful for your updated assessment before the discussion period ends.

Thank you for your consideration.

Reviewer_VZSQOpenReview ↗
Rating
4
Confidence
2
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

The paper concerns routing foundation models applied to the vehicle routing problem and its variants. The authors developed a multi-agent interface organized around vehicle and partial-route states and route–customer extensions. They evaluated weight-frozen transfer under supplied constraint features and feasibility masks, and fine-tuning with new vehicle attributes and objectives. Frozen reuse gives in-distribution costs comparable to the strongest baseline, a 17.19% mean gap on 32 unseen variants at N=100 against 34.89% for that baseline, with the lowest gap on 28 of them, and the lowest neural gap on 37/65 CVRPLib instances. At 1M fine-tuning samples, the pipeline has lower costs than both adapted multi-task baselines in all min-max cells and in three of four min-sum cells. The pretrained fine-tuning at 200K target exposures reaches a lower mean cost than scratch training at 1M in each of three fleet settings over three downstream seeds.

Critical strengths

The paper is well written, and the results seem to be very good. I also appreciate the design of experiments, as well as including a comprehensive ablation study and the appendix.

Critical weaknesses

I did not identify critical weaknesses.

Questions for authors

I do not have any specific questions to the authors.

2 comments
AuthorsOpenReview ↗

Response to Reviewer VZSQ

We thank the reviewer for the time spent on our paper and for the positive assessment. We are glad that the paper was found well written, and that the experimental design, the ablation study and the appendix were considered valuable. The General Response summarizes the changes made in response to the other reviews: a corrected evaluation of our unseen-variant results at N=50, RF-TE and CCL re-evaluated with every depot encoded, RF-TE retrained with our distance prior, and a control that builds one route at a time with the same backbone. Our model remains below the compared baselines on all 24 multi-depot variants at both sizes, and the revised PDF reports both construction schedules in Table 4.

Area_Chair_san8OpenReview ↗

Irresponsible Reviewer

Dear Reviewer VZSQ and authors,

Unfortunately, this is a super irresponsible review.

So I will not consider the rating. Please focusing on the comments of other reviewers.

Best, AC

Reviewer_jAXkOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies the pre-training and transfer learning of multi-variant VRPs, maintaining persistent tokens and dynamic states for multiple routes, and jointly selecting feasible route-customer or route-depot pairings at each step. The method combines existing joint decoding and agent communication, incorporating −log(distance) into the scoring, and conducting multi-start training by changing the number of active slots. After pre-training on 16 CVRP variants, parameters were frozen and tested on 32 unseen MD/MB variants and CVRPLib, with fine-tuning then performed separately for min-sum and min-max HCVRPs. Improvements to unseen variants are mainly focused on multi-depot tasks, and comparisons with the same architecture and downstream training schemes also support the value of pre-training initialization.

Critical strengths
  1. Under the same architecture and downstream training scheme, pre-training initialization is superior to training from scratch, supporting its value for downstream learning.
Critical weaknesses
  1. This paper mainly applies the existing multi-agent route construction mechanism to multi-variant VRP pre-training, but lacks a comparison of route-by-route construction under the same backbone, prior and training conditions, and has not yet isolated the transfer benefits brought by this interface.
  2. The main advantages are concentrated in multi-depot tasks, but the baseline features and masks for MD/MB have not been verified to be consistent, and the comparison conditions still need to be confirmed.
Questions for authors
  1. Table 4 shows that distance prior has a large impact, but there is a lack of comparisons with the same prior applied to the baseline, so the independent benefits of the construction interface remain unclear. After adding the same −log(distance) in training and inference to RF-TE/CCL, what is the gap on unseen variants?
  2. How does the transfer performance of route-by-route construction work with fixed backbone, prior, training data, and budget?
  3. After unifying the input and feasibility rules for MD/MB, do the main transfer advantages still hold?
  4. In the random fleet min-sum problem, how do the solution qualities under the same time budget in this paper and RF-TE/CCL compare (Tables 16 and 25)?
  5. What is the quality of solutions under the same time budget for the complete and non-communication models (Tables 4 and 23)?
8 comments
AuthorsOpenReview ↗

Response to Reviewer jAXk (1/4): W1 and Q2, one-route-at-a-time control

We thank the reviewer for the careful review and for naming the controls that would settle each concern. We added controls for each question; CCL already uses a −log(distance) bias and is kept as published (Q1). The replies follow the order W1/Q2, Q1, W2/Q3, Q4, Q5; the changes in the revised PDF are listed in the General Response.

W1 (existing mechanism). The pair softmax comes from JAMPR and 2D-Ptr and the distance score from DAR; §2 and the text at Eq. (2) state this, and the paper claims neither as new. It adds route communication and allocation-driven multi-starts over persistent route-slot tokens. Its subject is pretraining one backbone across variants with this construction and measuring what is reused: frozen transfer to unseen constraints (Q1, Q3), fine-tuning to new vehicle attributes and objectives (Q4), and the pretrained-versus-scratch comparison that the reviewer lists as a strength. The control below shows that concurrent construction is not needed for frozen multi-depot transfer, and we withdraw that attribution.

W1/Q2. Route-by-route construction with the same backbone, prior, data and budget. We trained this control. It keeps our backbone, route-slot tokens, −log(distance) prior, training data, recipe (300 epochs, seed 1234) and evaluation (400 candidates), and changes the construction schedule, and with it what route communication can see: one route is open at a time. While a route is open, only its slot can act; when it returns to its depot, any slot can open the next route, so the depot (on HCVRP, the vehicle) of each new route is chosen jointly with its first customer in one (slot, target) softmax. With one open route there is no other route to communicate with, so route communication is restricted to the slot itself. No parameter is added or removed. We call this the one-route-at-a-time schedule. Neither schedule is better everywhere. Mean gap (%) on the Table 4 instances (N=50, same evaluator and instances):

ConstructionID16Unseen32MD24SD-MB8
Ours (concurrent, route communication)1.32711.74013.1007.662
− communication (Table 4)1.53411.56412.5698.552
One route at a time1.8209.88610.2698.735

Concurrent construction is lower on all 16 training variants and on 6 of the 8 unseen single-depot mixed-backhaul variants. The one-route-at-a-time schedule is lower on 22 of the 24 unseen multi-depot variants and on the unseen average (9.89% vs. 11.74%). Removing communication alone does not reach it on MD24 (12.57% vs. 10.27%). Both differences come mainly from variants with time windows (ID: 0.66% vs 1.45%; multi-depot: 13.00% vs 7.75%, lower on 12/12); without time windows the two schedules are within 0.5 pp in every group. Multi-depot transfer therefore does not come from concurrent construction. Within the concurrent schedule, the Table 4 ablations tie it to the geometric prior (removing it raises the gap on 24/24 multi-depot variants) and to the route-slot tokens on multi-depot variants with time windows (12/12; without time windows, removing them lowers the mean gap, on 8 of 12 variants, which we report in §5). Both are kept in the one-route-at-a-time control.

We also fine-tuned both schedules on HCVRP min-max (N=60, 1M target exposures, three fine-tuning seeds per model), each from its own N=50 pretrained model. There, self-only communication also hides the other vehicles' elapsed times, so we added a variant that starts from our pretrained model, keeps route communication and removes only concurrency. With five and seven vehicles, this variant has a higher makespan than ours in all three seeds; with three vehicles the differences change sign across seeds. Mean makespan with 1,280 candidates; in parentheses, the range over seeds of the mean paired difference to ours with the same seed:

ConstructionM=3M=5M=7
Ours (concurrent, route communication)6.72274.10663.0076
One route at a time, communication kept6.7245 (−0.01 to +0.11%)4.1151 (+0.19 to +0.26%)3.0178 (+0.30 to +0.45%)
One route at a time (control above)6.7205 (−0.08 to +0.03%)4.1192 (+0.20 to +0.43%)3.0288 (+0.54 to +0.84%)

The control above loses about twice as much at M=7.

The schedule is a trade-off: concurrent construction is better in distribution and, when fine-tuning starts from our pretrained model, on min-max makespan with five and seven vehicles, while one route at a time transfers better to unseen multi-depot variants. The paper keeps the concurrent model as its main model and reports the control next to it: in the revision, we add the one-route-at-a-time row to Table 4 and a paragraph to §5. Appendix E adds the per-variant and time-window results, the HCVRP min-max comparison and implementation checks.

AuthorsOpenReview ↗

Response to Reviewer jAXk (2/4): Q1 distance prior in the baselines; W2/Q3 multi-depot inputs

Q1. The same −log(distance) prior in the baselines. CCL already uses a −log(distance) bias in training and inference, added inside a decoder cross-attention layer and switched on stochastically per step (routefinder/models/decoder.py, lines 394–421 of its released code); we therefore keep CCL as published and did not retrain it with our term. RF-TE has no distance prior, so we retrained it with the same term as ours: −log(distance) added to its pointer logits before tanh clipping, in training and inference, with the official RF-TE recipe (N=50, 300 epochs) and no added parameter. We compare it with the official checkpoint under the same evaluator, files and 400 candidates. The prior helps RF-TE but does not account for our margin. Mean gap (%) on the 32 unseen variants at N=50, by baseline depot input (ours always encodes all depots):

Modeloriginal inputsall depots encoded (W2/Q3)
RF-TE36.5332.14
RF-TE + −log(distance)29.5421.52
CCL (own −log(distance) bias)27.5918.73
Ours without distance prior (Table 4)–17.99
Ours–11.74

The prior helps RF-TE substantially (−7.0 pp and −10.6 pp; lower gap on 29 of 32 variants, the other three being MB-TW variants within 0.4 pp), so it is a useful bias in both tested systems. With the same prior and all depots encoded, RF-TE remains at 21.52% against our 11.74%, and our model without the prior (17.99%) is already below RF-TE with it. This is a comparison between systems; W1/Q2 above separates the construction schedule within our model. We add this comparison to Appendix C.

W2 / Q3. MD/MB inputs and feasibility rules of the baselines. Thank you for this question; it identified a real difference in the depot inputs.

Original protocol. The baseline numbers in Table 8 are those reported by CCL, obtained with the official checkpoints and CCL's evaluator. We evaluate on CCL's test instances (regenerating them with CCL's script reproduces our files bit for bit) against the same PyVRP references. RouteFinder's MTDVRP environment, used for RF-TE and CCL, applies the same feasibility rules as ours (time windows, return-to-depot time, route-length limit, linehaul/backhaul capacity, classical and mixed backhaul). For MD, both environments let each route start at any depot and close it at the depot it started from, so they admit the same set of solutions: in ours, slots are bound to depots in round-robin order and a slot that has returned can start another route, so any depot can start any number of routes. MB inputs are also equal: no model receives the mixed-backhaul class as input, and in all of them it is enforced only by the feasibility mask.

Difference in depot inputs. The released RF-TE and CCL checkpoints use RouteFinder's single-depot embedding. It embeds node 0 as the depot and the other depots as zero-demand customers, even though the mask treats them as depots. Our route slots carry every depot.

Re-evaluation with all depots encoded. We re-evaluated both baselines with every depot embedded through each checkpoint's own depot projection, with no parameter added or changed. No model, ours included, was trained with multiple depots. Files, masks and candidate budgets are unchanged (400 at N=50, 800 at N=100). CCL results are averaged over three seeds because its decoder is stochastic. Both baselines improve with all depots encoded; ours stays lower on all 24 MD variants at both sizes. Mean gap (%) on the 24 MD variants at N=50 (N=100 is in Appendix C):

Modeloriginal inputs (reported)all depots encoded
RF-TE45.6739.82
CCL33.9222.11
Ours–13.10

Part of the original MD margin therefore came from the baselines' depot encoding. Our MD margin over CCL is 9.0 pp at N=50. Over all 32 unseen variants, with the single-depot MB results unchanged, CCL with all depots encoded averages 18.73% (N=50) and 27.21% (N=100), against our 11.74% and 17.19%. The abstract, §1 and the caption of Table 1 give this all-depot mean next to the published one (34.89%). The number of variants on which our gap is the lowest of the compared systems (28/32 at N=100, 27/32 at N=50) is the same under both inputs. Appendix C reports, per variant, both baselines with all depots encoded, next to the numbers reported by CCL. CaDA keeps its reported numbers, since its checkpoint is not public. We also replace the statement in §5 that baseline MD/MB features were not verified.

AuthorsOpenReview ↗

Response to Reviewer jAXk (3/4): Q4, HCVRP min-sum at matched inference time

Q4. At matched time, our model is 0.26–0.48% below RF-TE and within about 0.1% of CCL. Table 25 is not a controlled timing, so we measured cost against inference time for the three 1M fine-tuned models. Checkpoints, test files, augmentations and the validity checker are those of Table 16; besides the number of candidates (160 to 3,840), only the sampling call changes. Our model and RF-TE draw all samples of an augmentation in one call (in Table 16, our model used blocks of at most 60). CCL draws them in blocks of at most 60 starts: with one call, its released protocol and the one used in Table 16, its cost is lowest at 640 candidates (15.716 at 41.6 s) and rises beyond that (15.719 at 1,280 candidates and 46.8 s). Times below are rollout times on one A100 after warm-up, measured on 256 instances with each model's fastest of three batch sizes and scaled to 1,280 test instances. Costs are averaged over the three fleets; at 1,280 candidates the one-call costs agree with Table 17 within 0.003.

CandidatesOurs time (s)Ours costRF-TE time (s)RF-TE costCCL time (s)CCL cost
16034.115.73330.015.81340.915.765
32041.315.71037.115.78640.815.733
64069.715.68952.615.76183.115.707
1,280171.415.66983.515.740124.715.686
2,560––146.315.722250.515.668
3,840––210.615.712333.915.660

We report our model up to 1,280 candidates, the budget of Table 16. Up to 320 candidates, one block holds all samples of an augmentation, so those CCL rows are one-call runs. Below, improvements are paired instance improvements with 95% instance-bootstrap intervals, the statistic of Table 16.

Against RF-TE, our model is lower at every time. Against the RF-TE run with the nearest time (37–146 s), the improvement is 0.32–0.48%. Against the RF-TE run with at least our time, it is 0.26–0.33%. RF-TE needs 3,840 candidates and 210.6 s to match our 320-candidate run at 41.3 s (0.004% [−0.021, 0.030]).

CCL is the stronger baseline. At about 41 s, the shortest time at which CCL runs, our 320-candidate run is essentially on par with the one-call 640-candidate CCL run (0.028% [0.002, 0.056] lower). At 70 s, our 640-candidate run is 0.102% [0.076, 0.128] lower than CCL with the same 640 candidates (83 s). At 171 s, our 1,280-candidate run is 0.094% [0.069, 0.119] lower than CCL with the same 1,280 candidates (125 s), 0.024% [−0.001, 0.048] higher than CCL with 2,560 candidates (251 s), and 0.075% [0.051, 0.099] higher than CCL with 3,840 candidates (334 s). Below 41 s there is no CCL run, and our 160-candidate run at 34.1 s is 0.12% above the one-call 640-candidate CCL run.

The margins of Tables 16 and 17 are therefore measured at equal candidates and with CCL's released one-call sampling. With one sampling call per augmentation, our model takes 3.7 times the time of CCL and 2.1 times that of RF-TE (171.4 s, 46.8 s and 83.5 s). At matched time, the margin over RF-TE remains 0.26–0.48%, and our model and CCL are within about 0.1% of each other. In the revision, we add this curve and the paired comparisons to Appendix F. We also state in §5 and Appendix D that the min-sum comparison is at equal candidates and refer to this curve, give the 1,280-candidate budget in §7, and note in Table 25 that it is not a controlled timing.

Comments on the paper

3 comments
AuthorsOpenReview ↗

General response: summary and changes in the revised PDF

General response. We thank the three reviewers for their careful reading and concrete questions. They led to one correction of our evaluation and to several new controls. The main points are:

  • Corrected unseen evaluation (dxBH). Our N=50 values in Table 8 were produced by an earlier version of our evaluation script that predates the multi-depot slot layout of Section 4.4, and our gap there was computed from mean costs rather than per instance. With the current script and per-instance gaps, our mean gap on the 32 unseen variants at N=50 is 11.74% instead of 13.97% (slot layout 2.1 pp, gap computation 0.1 pp).
  • One-route-at-a-time control (jAXk). A control that keeps our backbone, prior, data and recipe and builds one route at a time changes our attribution of multi-depot transfer (summarized below).
  • Baseline inputs on multi-depot variants (jAXk). The released RF-TE and CCL checkpoints embed only one depot. With every depot encoded, both baselines improve: CCL's mean gap on the 32 unseen variants falls from 27.59% to 18.73% at N=50 and from 34.89% to 27.21% at N=100, against our 11.74% and 17.19%. Our model remains lower on all 24 multi-depot variants at both sizes.
  • Distance prior (dxBH, jAXk). Our −log(distance) term is a case of DAR's distance score; we cite DAR and state this next to Eq. (2). RF-TE retrained with the same prior improves but stays above our model, including our model trained without the prior.
  • Matched inference time (jAXk). We add matched-time comparisons for HCVRP min-sum and for the model without route communication.

What the new controls show. The one-route-at-a-time control changes our interpretation: concurrent construction is not necessary for the observed multi-depot transfer. With the same backbone, prior, data and training budget, building one route at a time gives a 9.89% mean gap on the 32 unseen variants at N=50, against 11.74% for concurrent construction, while concurrent construction is lower on all 16 training variants and on 6 of the 8 unseen single-depot variants. We withdraw the attribution of multi-depot transfer to concurrency and report both schedules in Table 4.

  • Transfer holds under both schedules. At N=50, both schedules are below RF-TE retrained with the same prior (21.52%) and CCL (18.73%), each with all depots encoded. This is a comparison between systems that also differ in backbone and recipe, and our experiments do not isolate which shared component explains the gap.
  • The schedule is a trade-off. Concurrent construction is better in distribution (1.33% vs. 1.82%), and when fine-tuning starts from our pretrained model, removing concurrency raises min-max HCVRP makespan with five and seven vehicles (0.2% and 0.3%). One route at a time transfers better to unseen multi-depot variants with time windows (7.75% vs. 13.00%); without time windows the two schedules are within 0.5 pp.
  • Adaptation with few target samples. On min-max HCVRP, within our architecture and recipe, 200K target exposures from the pretrained weights reach a lower three-seed mean cost than 1M from scratch in every fleet setting, and updating only the projections (3.4% of the parameters) is below scratch at every evaluated budget from 100K to 1M.

Changes in the revised PDF

Added or changed text is in blue; removed text is not shown and is listed here.

  • Our N=50 unseen-variant results replaced by the current-script evaluation of Table 4 (§5, §6, Appendix C, Table 8, per-variant table), and the statements based on the earlier numbers updated or removed (§5, Appendices C and E).
  • Candidate budget for unseen evaluation at N=100 corrected to 800 for every method (§5, Appendix C).
  • Earlier multi-depot slot layout and gap computation stated (Appendix C).
  • Baseline multi-depot inputs and the all-depot re-evaluation (abstract, §1, §5, Table 1, Appendix C).
  • RF-TE retrained with −log(distance) (Appendix C).
  • DAR in the related work, at Eq. (2), and a CVRPLib comparison with DAR's score (§2, §4, Appendix C).
  • Full model and model without communication at matched inference time (§5, Appendix F).
  • HCVRP min-sum cost against inference time; Table 25 marked as not a controlled timing; 1,280-candidate budget stated in §7 (§5, §7, Appendices D and F, Table 25).
  • One-route-at-a-time control in Table 4, §5 and Appendices B and E, with the HCVRP min-max comparison.
  • Statements attributing transfer to the construction revised, and the limitation on a sequential configuration replaced (§1, §4–§7).
  • Removed, since they came from the earlier evaluation: the share of our margin over CCL attributed to the prior (37%; §5, Appendix E), the earlier component ablation with the PARCO-style decoder (Appendix E), and the pretraining-seed SD of the unseen mean (Appendix C).

Dear Reviewers,

The authors have posted their responses. Please take a look and respond to the authors.

Best, AC

Dear Reviewers,

The authors have posted their responses. Please take a look and respond to the authors.

Best, AC

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

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