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Under review as a conference paper at ICLR 2027

Bridging Local Observation and Global Simulation in Closed-Loop Traffic Modeling

Abstract

Autoregressive traffic simulators learn from local, ego-centric driving logs but must generate globally coherent multi-agent interactions. Limited observation range leaves the context incomplete for non-ego agents, particularly those far from the ego vehicle. Simulators may therefore learn actions without observing the conditions that induced them and reproduce those actions in contexts where they are inappropriate—a problem we term the ***local-to-global context mismatch***. We introduce ***CRAFT***, **C**ontextual p**R**eference **A**lignment **F**ramework for **T**raffic Simulation, a lightweight, plug-and-play framework that uses closed-loop rollouts to expose and rectify such behaviors. Agnostic to the base simulator’s architecture, motion prior, and training strategy, CRAFT operates post hoc without retraining or modifying the simulator. CRAFT labels grouped rollouts using traffic-rule and driving-quality criteria, then trains a separate Contextual Preference Evaluator (CPE) through contrastive preference learning over normal and failure cases within trajectories and across rollouts. At inference, the CPE uses lookahead to evaluate candidate scene evolutions and reweights action probabilities toward contextually appropriate behavior. Across three state-of-the-art simulators on the Waymo Open Motion Dataset, CRAFT reduces scene-level collision, offroad, and traffic-violation rates by up to 31.2%, 14.9%, and 33.2%, respectively, while improving motion realism. These results ***establish contextual preference alignment*** as a general and efficient mechanism for mitigating local-to-global mismatch ***across heterogeneous traffic simulators***.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Traffic Simulation, Autonomous Driving, Preference Alignment, Multi-agent Motion Generation

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_w4cxOpenReview ↗
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Paper summary

To address the local-to-global (L2G) context mismatch problem in autoregressive traffic simulators, this paper propose CRAFT, a plug-and-play, simulator-agnostic framework that trains a Contextual Preference Evaluator (CPE) on grouped closed-loop rollouts with traffic-rule and driving-quality labels, then reweights candidate actions via one-step lookahead at inference without retraining the base models. On the Waymo Dataset, CRAFT reduces scene-level collision, offroad, and traffic-violation rates across three state-of-the-art simulators (SMART, CAT-K, RLFTSim).

Critical strengths
  • The paper formalize the L2G mismatch with a formal derivation showing that fitting incomplete-context demonstrations yields a marginal distribution that necessarily diverges from scene-specific behavior, and validates the causal role of context via a controlled ablation that varies visible agents during training.
  • By decoupling behavioral correction (CPE) from the motion prior (base simulator), a single CPE checkpoint improves three architecturally distinct SOTA simulators without retraining or modifying them. This cross-model transferability and low deployment cost is practically valuable in traffic simulation.
Critical weaknesses
  • CRAFT is a re-ranking mechanism, not a generator. It can only select among the K=32 candidate actions the base simulator proposes. If the proposal distribution contains no suitable action, CRAFT cannot create it. The improvement is thus bounded by the base model’s coverage and may fail entirely on long-tail extreme scenarios.
  • Test-time guidance evaluates single-step outcomes, so it cannot anticipate multi-step cascading effects, which is a conservative action now may steer the scene into a more dangerous interaction later. No experiments vary lookahead depth (2 or 5 steps) to test whether deeper planning would help.
  • All experiments run only on the Waymo Open Motion Dataset. No validation on additional dataset such as nuScenes, Argoverse. It is not clear whether CPE’s learned notion of “contextual appropriateness” transfers across geographies.
  • CPE’s supervision derives entirely from a hard-coded rule-based auto-labeler. These rules are noisy, e.g., a legitimate yield-to-pedestrian or courtesy stop could be mislabeled as abnormal stopping, and they cannot capture subtler misbehavior (tailgating, unsignaled lane changes). The paper reports no human-verified label accuracy nor an analysis of how label noise affects CPE.
  • The default inference latency is very high, while low latency comes from chunked batching of 32 candidates and sacrifices some diversity. For massively parallel simulation (hundreds of agents), running K lookahead evaluations every step still imposes significant aggregate compute.
Questions for authors
  • How robust is CRAFT when the base simulator's proposal distribution is itself largely dominated by inappropriate actions. If a base simulator were poor, could CRAFT still provide meaningful improvement, or does it fundamentally inherit the base model’s blind spots?
  • What does the learned contextual appropriateness actually capture beyond the six hard-coded rules? Since CPE is trained only on rule-based labels, can it generalize to judge behaviors the auto-labeler never explicitly encodes? Could a human-annotated or VLM-derived preference set change what the evaluator learns?
  • How sensitive are the results to the choice of the auto-labeling criteria and the weighting hyperparameters?
3 comments

Thank you for the constructive questions about candidate coverage, longer-horizon interactions, transfer, and supervision. We have submitted the revised manuscript, with changes highlighted in blue. And we address each concern below.

W1/Q1. How robust is CRAFT when the base simulator's proposal distribution is itself largely dominated by inappropriate actions. If a base simulator were poor, could CRAFT still provide meaningful improvement, or does it fundamentally inherit the base modelʼs blind spots?

R1. Like other proposal-based test-time methods, CRAFT relies on the base model's action distribution. At K=32K=32, CAT-K achieves a 95.14% logged-token recall on the evaluated logged states (Appendix F, Fig. 15), indicating that its candidate pool usually contains demonstrated actions available for selection.

We further examine the distribution of unguided CAT-K closed-loop scores to assess correction when the base simulator performs poorly. The rare, low-scoring group contains 31 of the 1,000 scenes (3.10%). Despite the poor baseline performance in this group, CRAFT improves its average score by 14.20 points, the largest gain among the three groups, while also improving the intermediate and common groups.

Scene groupCAT-K score rangeScenesCAT-KCRAFTGain (points)
Rare<333118.0632.26+14.20
Intermediate33–6622649.4759.00+9.53
Common>6674386.6491.11+4.47
All0–1001,00076.1082.00+5.90

We have added this breakdown to Fig. 9(a) and its analysis to §5.6.

Appendix E, Fig. 13, shows CRAFT recovering from an initial perturbation and maintaining road alignment through a sharp turn. By selecting better available actions, CRAFT improves subsequent scene states even when the base rollout is poor. Appendix F, Fig. 14 shows that recovery remains limited when suitable candidates are persistently absent.

W2. Test-time guidance evaluates single-step outcomes, so it cannot anticipate multi-step cascading effects, which is a conservative action now may steer the scene into a more dangerous interaction later. No experiments vary lookahead depth (2 or 5 steps) to test whether deeper planning would help.

R2. We agree that one-step scoring does not explicitly evaluate all later consequences. Following your suggestion, we compare one-, two-, and three-step lookahead with candidate chunk size fixed at 4.

Lookahead stepsCollision (%) ↓Offroad (%) ↓Traffic violations (%) ↓Closed-loop score ↑Full step (ms) ↓
110.8016.6026.6082.00131.166
210.1015.5026.8082.53213.775
39.8016.2026.1082.63297.007

Deeper lookahead adds substantial cost for only marginal benefit: three steps require 2.26 times the runtime for a 0.63-point score gain. With a fixed sampling budget, the longer horizon still covers only a small subset of possible future interactions, limiting the additional information available for choosing the current action. These results support one-step lookahead as our practical default. CRAFT reevaluates candidates after every executed action, allowing repeated correction as the scene evolves.

W3. All experiments run only on the Waymo Open Motion Dataset. No validation on additional dataset such as nuScenes, Argoverse. It is not clear whether CPEʼs learned notion of “contextual appropriateness” transfers across geographies.

R3. The WOMD-trained CPE also improves simulation on Argoverse without adaptation. We use WOMD as the primary benchmark because its scale, diverse driving interactions, and dedicated Sim Agents task make it particularly well suited to multi-agent simulation, whereas the relevant Argoverse and nuScenes benchmarks primarily target trajectory forecasting.

Following your suggestion, we evaluate the WOMD-trained CAT-K simulator and CPE on 500 randomly sampled Argoverse scenes, without training or tuning on Argoverse.

MetricCAT-KCRAFTRelative reduction (%)
Collision rate (%)30.0021.8027.33
Offroad rate (%)49.0041.2015.92

Both rates improve under this dataset shift, supporting the transfer of learned contextual preferences beyond WOMD. Additionally, traffic violations are not evaluated because these inputs lack traffic-signal states. We have added the results as Table 3 and discussed this transfer in §5.6.

W4. CPEʼs supervision derives entirely from a hard-coded rule-based auto-labeler. These rules are noisy, e.g., a legitimate yield-to-pedestrian or courtesy stop could be mislabeled as abnormal stopping, and they cannot capture subtler misbehavior (tailgating, unsignaled lane changes). The paper reports no human-verified label accuracy nor an analysis of how label noise affects CPE.

R4. We agree that rule-based annotations inevitably contain some noise. We therefore report the results of a manual audit of 480 randomly sampled rollouts from the 480,000 generated rollouts. Missed abnormalities occurred in 17 rollouts (3.54% of the audited sample): 14 abnormal stops and three traffic-signal violations. The relatively few errors found in the audit, together with the training ablation and closed-loop improvements (Fig. 5 and Table 1), suggest that the observed label noise does not pose a major obstacle to effective CPE training and online guidance.

W5. The default inference latency is very high, while low latency comes from chunked batching of 32 candidates and sacrifices some diversity. For massively parallel simulation (hundreds of agents), running K lookahead evaluations every step still imposes significant aggregate compute.

R5. CRAFT supports low-latency guidance: with a candidate chunk size of 32, lookahead takes only 3.97 ms (Fig. 8(a)), and a full simulation step takes 43.11 ms (Table 13).

Chunking partitions the candidate action pool, not the agents within a scene. Each candidate retains all simulated agents, and all K=32K=32 candidates are evaluated and normalized over the complete pool. For the same candidate samples and sampling randomness, different chunk sizes are mathematically equivalent and yield the same action-selection results, without sacrificing diversity.

The full-step latency and memory usage by agent count are:

Agents per sceneFull-step latency (ms)Memory (MiB)
10–3935.0884.1
40–7969.62988.0
80 or more91.05449.2

Even for scenes with 80 or more agents, the average full-step latency is 91 ms, which we consider acceptable for closed-loop simulation. Further runtime analysis is provided in §5.5 and Appendix F.2 (Table 13).

Q2. What does the learned contextual appropriateness actually capture beyond the six hard-coded rules? Since CPE is trained only on rule-based labels, can it generalize to judge behaviors the auto-labeler never explicitly encodes? Could a human-annotated or VLM-derived preference set change what the evaluator learns?

R6. CPE learns continuous, context-dependent preferences from the rule labels, rather than adding new behavioral criteria beyond its supervision. The six rules cover frequent failures observed in our rollouts. Relative preference learning provides finer scores for candidate selection, and Fig. 7(a) shows sensitivity to interaction context.

The preference-learning mechanism is not restricted to this source. Future work could use Human and VLM-generated comparisons to supply interaction judgments that hand-coded rules do not readily express, with human spot checks to verify reliability. Such preferences could change what CPE learns by broadening its supervision.

Q3. How sensitive are the results to the choice of the auto-labeling criteria and the weighting hyperparameters?

R7. The choice of auto-labeling criteria can influence what CPE learns. We selected six criteria to capture the main forms of contextual abnormality observed in our rollouts, enabling CPE to learn the corresponding behavior–context mismatches. The results demonstrate that this choice provides a reasonable implementation of CRAFT, with promising performance in mitigating the L2G gap through contextual correction. Further investigation of the criteria and their thresholds could help refine the supervision provided to CPE and improve CRAFT’s performance.

In terms of weighting hyperparameters, for training, Table 5 reports the loss weights, and Fig. 5 ablates the corresponding objectives. Both intra-trajectory and inter-rollout preference learning improve performance, with their combination achieving the best result. For inference, we analyze two settings: β=2\beta=2 gives the best tested behavioral performance; stronger guidance worsens all three event rates (Fig. 8(b)). CRAFT improves over the matched CAT-K baseline at every tested KK, with its highest closed-loop score at K=32K=32 (Fig. 8(c)).

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Request for Reply

Dear Reviewer w4cx,

Thank you for your review and helpful suggestions. We’d like to highlight four results from our revision:

  • Re-ranking helps even when the base simulator struggles, with the largest gain in the lowest-scoring scenes.
  • One-step lookahead offers the better runtime trade-off, as deeper lookahead yields only modest gains.
  • Zero-shot guidance on Argoverse reduces collisions and offroad events.
  • Latency and GPU memory are measured across agent counts, with batching preserving the full candidate pool.

If you have any further concerns, please let us know and we are happy to address them. We would welcome any further feedback and would appreciate your taking these results and clarifications into account in your final assessment.

Best regards, Submission25923 Authors

Reviewer_o6LLOpenReview ↗
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Paper summary

The paper argues that traffic simulators trained on ego-centric logs can learn actions whose triggering context was never recorded, and then repeat those actions in simulated scenes where they are unjustified. The authors call this the local-to-global (L2G) context mismatch. CRAFT is a post-hoc fix that leaves the simulator frozen. It labels CAT-K closed-loop rollouts with rule-based criteria (collision, offroad, traffic violations, abnormal stopping, and others). On these labels it trains a Contextual Preference Evaluator (CPE) with BCE plus intra-trajectory and inter-rollout preference losses. At inference, CPE reweights each agent’s top-K candidate actions through one-step lookahead. On WOMD, a single CPE reduces event rates for SMART, CAT-K and RLFTSim (closed-loop score +2.7 to +6.0). Supporting results include ablations, an offline-selection vs. online-guidance comparison, WOSAC results, a human study, and latency measurements.

Critical strengths

The paper identifies a real and under-discussed problem in log-trained traffic simulators and proposes a fix that is simple and practical. CRAFT needs no retraining, adds about 4 ms per step, and one CPE trained on CAT-K rollouts consistently reduces collision, offroad and traffic-violation rates on three simulators. Two results stand out to me. Online guidance clearly beats offline best-of-N selection with the same evaluator (Table 2), so step-wise correction does more than filtering. And human raters prefer CRAFT over CAT-K in 44.8% of judgments vs. 19.0%, which is evidence that does not depend on the rule-based metrics.

The paper is also transparent about its trade-offs. It reports the unfavorable WOSAC numbers, analyzes a failure case caused by missing candidates, and runs reasonable ablations of the CPE objectives and of β, K and data size.

Critical weaknesses

The main evaluation is close to circular. CPE learns from a rule-based labeler whose criteria largely match the event definitions behind the closed-loop score, so gains on that score are partly expected. On WOSAC, the default β=2 lowers CAT-K’s composite realism from 0.765 to 0.719, the kinematic score drops noticeably, and minADE rises from 1.99 to 3.34 m. The authors’ explanation, that log matching penalizes contextual corrections, is plausible for some cases. It does not fully account for the worse acceleration likelihoods and the reduced diversity, which suggest the guidance narrows the behavior distribution. For this reason I read “improving motion realism” in the abstract as overstated. Results also come from 2% of the validation split with no variance reported.

The link between the L2G motivation and the method is somewhat loose. CPE learns rule compliance and would equally correct generic compounding errors, and the paper does not show that the errors it fixes come from missing context, for example by analyzing error rates against distance from the logging vehicle. Similarly, “architecture-agnostic” is a strong label, since all three simulators share the SMART tokenized architecture and CPE uses CAT-K’s encoder. I consider these mainly framing issues rather than flaws in the method itself.

Questions for authors
  1. The rule-based labeler, used directly as online guidance, does worse than no guidance (75.83 vs. 76.10 in Table 1). Yet the same rules are the best offline selector (Table 2), and CPE, which is trained to imitate them, helps substantially. What explains this gap? Are the step-level labels computed with future information, for example marking a step negative because it leads to a later collision? If so, CPE’s advantage is mainly anticipation, and a multi-step rule-based lookahead would be the fair baseline.

  2. The abstract says the mismatch mainly affects agents far from the ego vehicle. Can you report event rates as a function of distance from the logging vehicle, or another proxy for missing context, for both the base simulator and CRAFT? This would be the most direct test that the errors CRAFT corrects come from L2G and not from generic compounding errors.

  3. How do you reconcile the WOSAC drop at β=2, especially in the kinematic terms and minADE, with the claim of improved realism? Table 8 shows that β=0.5 keeps WOSAC much closer to the base model. Could you report the Table 1 metrics at β=0.5 and β=1, so that the trade-off between event rates and WOSAC realism is visible at the same settings?

  4. All three simulators guided by CRAFT share the SMART tokenized architecture, and CPE uses CAT-K’s encoder. Can you show results on a simulator outside this family, such as GUMP, which is already in Table 1, or a diffusion-based model? Does a CPE trained on another simulator’s rollouts transfer equally well?

  5. How many scenes and rollouts per scene are used for Table 1, and how stable are the results across random seeds? For the human study, who were the evaluators? Were the pairs blinded and shown in random order? What was the inter-rater agreement?

3 comments

Thank you for the detailed assessment and for recognizing the value of online correction and the human evaluation. We have submitted the revised manuscript, with changes highlighted in blue. And we address the evaluation, mechanism, and transfer questions below.

W1. The main evaluation is close to circular. CPE learns from a rule-based labeler whose criteria largely match the event definitions behind the closed-loop score, so gains on that score are partly expected. On WOSAC, the default β =2 lowers CAT-Kʼs composite realism from 0.765 to 0.719, the kinematic score drops noticeably, and minADE rises from 1.99 to 3.34 m. The authorsʼ explanation, that log matching penalizes contextual corrections, is plausible for some cases. It does not fully account for the worse acceleration likelihoods and the reduced diversity, which suggest the guidance narrows the behavior distribution. For this reason I read “improving motion realism” in the abstract as overstated. Results also come from 2% of the validation split with no variance reported.

R1. Action-level supervision is distinct from scene-level closed-loop evaluation. CPE learns agent–time labels and preferences from generated rollouts; evaluation independently counts collision, offroad, and traffic-violation events after complete closed-loop simulations on held-out scenes. It reuses neither training labels nor CPE predictions. The rules and metrics intentionally target overlapping behaviors, but the test measures whether those behaviors actually improve during generation. Additionally, the human preference results provide complementary evidence independent of the rule-based metrics (Table 11).

Our realism claim concerns the simulated scene as a whole. WOSAC directly evaluates a small designated subset—the ego vehicle and up to eight WOMD prediction targets—within scenes containing tens to hundreds of agents. Other agents affect relevant interaction terms but do not all receive their own feature-likelihood evaluation. Therefore, lower likelihoods for this subset do not by themselves establish poorer realism throughout the scene. Our Realism score instead pools motion features across all valid moving agents, which we consider a fairer basis for assessing scene-wide contextual correction. It improves together with the behavioral event rates; Appendix D.1–D.3 explains the difference in evaluation targets.

We acknowledge some reduction in behavioral diversity: CAT-K's pairwise endpoint dispersion decreases from 9.54 to 8.24 m, while remaining comparable to the other base simulators (Table 10). We consider this reduction acceptable given the accompanying improvements in behavioral rationality. The worse acceleration likelihoods and minADE reflect poorer matching to the designated agents' logged futures; the contextual example in Appendix D.1 illustrates why the objectives can differ, without attributing every kinematic decrease to that example.

W2. The link between the L2G motivation and the method is somewhat loose. CPE learns rule compliance and would equally correct generic compounding errors, and the paper does not show that the errors it fixes come from missing context, for example by analyzing error rates against distance from the logging vehicle. Similarly, “architecture-agnostic” is a strong label, since all three simulators share the SMART tokenized architecture and CPE uses CAT-Kʼs encoder. I consider these mainly framing issues rather than flaws in the method itself.

R2. CRAFT incorporates additional prior knowledge at test time to mitigate the effects of learning from incomplete-context demonstrations. Because correction depends on behavior–context compatibility, it can address both L2G-related errors and contextually inappropriate behavior arising from error accumulation or other causes. The controlled Base/CRAFT context experiment in Fig. 2 and §3 supports this motivation, as detailed in R4 below. To strengthen the evidence beyond the SMART family, we have added GUMP to Table 1 and discuss it in §5.2. This directly tests transfer to a different simulator family; the adaptation and results are described in R6 below.

Q1. The rule-based labeler, used directly as online guidance, does worse than no guidance (75.83 vs. 76.10 in Table 1). Yet the same rules are the best offline selector (Table 2), and CPE, which is trained to imitate them, helps substantially. What explains this gap? Are the step-level labels computed with future information, for example marking a step negative because it leads to a later collision? If so, CPEʼs advantage is mainly anticipation, and a multi-step rule-based lookahead would be the fair baseline.

R3. Offline selection judges completed outcomes; online guidance must change the actions that produce them. The auto-labeler checks realized rule outcomes directly, avoiding learned classification errors, and obtains a higher offline-selection score than CPE (78.33 vs 78.07). Online, however, the scores must reshape action probabilities before the remaining rollout is generated. Accurate binary classification therefore need not produce effective online guidance. We find two limitations of directly using the binary rules:

(1) Most decisions provide no candidate differentiation. In 74.60% of decisions, all candidates share the same label. Their common guidance multiplier cancels during normalization, leaving the action distribution unchanged.

ModelAll labels = 1All labels = 0
CAT-K71.29%3.31%

(2) Binary labels provide coarse probability adjustments. Even with mixed labels, relative probabilities within each class remain unchanged. CPE's continuous contextual preferences permit finer distinctions and produce substantially larger mean probability adjustments.

ModelAuto-labeler mean probability adjustmentCPE mean probability adjustment
CAT-K0.1671%9.8070%

In contrast to autolaber, CPE provides continuous, differentiable contextual scores, enabling CRAFT to reweight candidate actions before each step is executed. This repeated correction helps prevent the rollout from progressively entering low-scoring contexts.

The step labels do not mark an action negative merely because a failure occurs later. They only use the evaluated current state. Online auto-labeler guidance and CPE evaluate the same one-step candidate scene state as shown in Algorithm 1.

Q2. The abstract says the mismatch mainly affects agents far from the ego vehicle. Can you report event rates as a function of distance from the logging vehicle, or another proxy for missing context, for both the base simulator and CRAFT? This would be the most direct test that the errors CRAFT corrects come from L2G and not from generic compounding errors.

R4. Following your suggestion, we use the number of visible training agents as a controlled proxy for missing context: more visible agents mean less missing context. We vary only agent visibility and evaluate each base simulator with and without CRAFT.

Visible training contextCollision Base / CRAFT (%)Offroad Base / CRAFT (%)Traffic violations Base / CRAFT (%)
Ego only42.80 / 25.2023.80 / 21.6046.20 / 35.10
Ego + 8 agents24.30 / 17.8022.40 / 21.3038.60 / 30.70
Ego + 32 agents22.00 / 15.5019.40 / 19.2036.50 / 29.20
Ego + all agents22.80 / 14.4017.80 / 17.4035.70 / 27.10

Providing more training context reduces all three base-model event rates relative to ego-only training. CRAFT further reduces collision, offroad and traffic violations in every context setting, with the largest reductions when the most context is missing (ego-only). These results support contextual guidance for mitigating errors associated with incomplete training context. We have added the paired comparison to Fig. 2 and its analysis to §3.

Q3. How do you reconcile the WOSAC drop at β =2, especially in the kinematic terms and minADE, with the claim of improved realism? Table 8 shows that β =0.5 keeps WOSAC much closer to the base model. Could you report the Table 1 metrics at β =0.5 and β =1, so that the trade-off between event rates and WOSAC realism is visible at the same settings?

R5. We report the requested settings below.

Guidance scale β\betaSpeed JSD ↓Angular-speed JSD ↓Nearest-agent-distance JSD ↓Realism score ↓Collision (%) ↓Offroad (%) ↓Traffic violations (%) ↓Closed-loop score ↑
Unguided1.022.960.531.5015.7019.5036.5076.10
0.51.013.050.681.5813.7019.5032.1078.23
10.992.820.741.5211.9018.5028.7080.30
20.922.200.691.2710.8016.6026.6082.00

WOSAC exhibits a trade-off between log matching and behavioral improvement, whereas our proposed metrics show improvements in both motion realism and behavioral rationality across all valid moving agents at the default guidance scale.

Q4. All three simulators guided by CRAFT share the SMART tokenized architecture, and CPE uses CAT-Kʼs encoder. Can you show results on a simulator outside this family, such as GUMP, which is already in Table 1, or a diffusion-based model? Does a CPE trained on another simulatorʼs rollouts transfer equally well?

R6. Following your suggestion, we have added GUMP to test transfer beyond the SMART family, using the same CPE checkpoint without retraining. All three JSD components and event rates improve under the matched protocol below.

ModelInferenceSpeed JSD ↓Angular-speed JSD ↓Nearest-agent-distance JSD ↓Realism score ↓Collision (%) ↓Offroad (%) ↓Traffic violations (%) ↓Closed-loop score ↑
GUMPTop-K1.383.290.721.8029.0025.8034.1070.37
GUMPCRAFT1.072.620.691.4627.8025.0030.2072.33

GUMP predicts at 2 Hz, whereas CRAFT requires 10 Hz trajectory input. We interpolate GUMP predictions to 10 Hz and compute all reported metrics on those trajectories. The results characterize this adapted comparison, not GUMP's native 2 Hz performance. The revised Table 1 replaces the previous native-frequency GUMP row with these matched results, and §5.2 discusses transfer beyond the SMART family.

We retain GUMP's agent-handling policy: some vehicles receive model-generated actions, others use velocity extrapolation, and others remain stationary. CRAFT modifies only the model-generated actions. Despite this restricted scope, the improvements demonstrate that contextual guidance also benefits a simulator outside the SMART family. Applying the current candidate-action guidance to a diffusion model would require adapting its inference interface.

For the training-source question, a matched comparison would require generating large rollout datasets from each simulator, annotating and manually auditing them, and retraining CPE under consistent settings. We cannot complete this process with comparable data quality within the rebuttal period and plan to study it in follow-up work.

Q5. How many scenes and rollouts per scene are used for Table 1, and how stable are the results across random seeds? For the human study, who were the evaluators? Were the pairs blinded and shown in random order? What was the inter-rater agreement?

R7. We evaluate 1,000 fixed validation scenes with 32 independently sampled rollouts per scene. Given the cost of closed-loop simulation, we follow CAT-K's subset-evaluation approach: its §5.3.2 and Fig. 4 compare 880 scenes with the full validation split and report consistent trends. The closed-loop scores below summarize stochastic rollout variability on our fixed scene set (mean ± SD).

Base simulatorBase scoreCRAFT score
CAT-K76.10 ± 1.0482.00 ± 0.79
SMART75.67 ± 0.8781.70 ± 0.82
RLFTSim76.60 ± 0.9179.33 ± 0.67

Three students with traffic-simulation backgrounds, independently judged the same 300 pairs. Model identities were hidden and presentation order randomized. All three agreed on 226 pairs (75.33% inter-rater agreement): 37 favored CAT-K, 105 favored CRAFT, and 84 were indistinguishable.

Reviewer_jSWNOpenReview ↗
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Paper summary

The paper identifies a specific failure mode of autoregressive traffic simulators trained on ego-centric driving logs — the local-to-global context mismatch. Because logged observations are restricted to the ego's sensor range, a learned behavior may persist in rollouts even when the surrounding condition that justified it has disappeared. §3 formalizes this as a gap between the logged marginal action distribution and the context- conditional distribution the simulator should match.

To mitigate this, the authors propose CRAFT, a plug-and-play Contextual pReference Alignment Framework:

  • At training time, grouped closed-loop rollouts from a frozen base simulator are automatically labeled with traffic/driving criteria, and a Contextual Preference Evaluator (CPE) is trained with three objectives: binary cross-entropy on label agreement (Eq. 9), intra-trajectory margin ranking of normal vs. failure segments (Eq. 10), and inter-rollout Bradley-Terry preference across alternative futures from the same initial scene (Eq. 11).
  • At inference, CPE scores one-step-lookahead candidate scenes and reweights the base simulator's action probabilities (Eq. 13).

On WOMD, CRAFT reduces per-agent collision, offroad, and traffic- violation rates, while also improving motion realism, across three different base simulators (SMART, CAT-K, RLFTSim) using a single CPE checkpoint without retraining the base simulators.

Critical strengths
  • Clean motivating experiment. Figure 2 varies only the training- time context size and shows a monotone decrease in event rates with more context. This is a clean argument for the problem's existence, independent of the proposed solution, and is a useful contribution on its own.
  • Practically appealing design. CRAFT is post-hoc and plug-and-play. A single CPE trained on CAT-K rollouts transfers to SMART and RLFTSim without retraining them, which is strong evidence of cross-simulator generality (Table 1).
  • Each training objective contributes. Figure 5 shows that cumulatively adding token-level scoring, rollout-level supervision, and intra/inter-rollout preferences improves both open-loop F1 and closed-loop score, with the full triple yielding the best result.
  • Inference cost is low. Fig. 7 reports 3.97 ms per step at chunk size 32, a 124× speedup over the rule-based auto-labeler (491.77 ms). This makes CRAFT realistically deployable in real- time simulators.
Critical weaknesses
  • The auto-labeler is doing much of the work. Table 1 shows that CAT-K + "Auto-labeler" already achieves closed-loop good score 75.83 vs. 76.10 for Top-K; CRAFT then adds ~6 points to 82.00. This is a real improvement, but the paper should distinguish more clearly between (a) the signal in the handcrafted criteria and (b) the learned CPE's ability to generalize beyond them. Table 2 has this comparison (AL rank 78.33 vs. CRAFT 82.00) but it should be highlighted earlier.
  • Cross-simulator transfer is uneven. CRAFT trained on CAT-K rollouts improves CAT-K by +5.90 and SMART by +6.03, but RLFTSim by only +2.73. The paper does not characterize when transfer succeeds or fails, which would be useful for practitioners deciding whether to adopt CRAFT for their simulator.
  • One-step lookahead is a notable approximation. CPE evaluates candidates by one-step marginal rollouts (l.265-269). Interactions that only become clearly inappropriate several steps later would be invisible to CRAFT. A multi-step lookahead study (even at K-step horizons for small K) would clarify this limitation.
  • Realism metric choice. The paper reports realism as a mean JSD over speed, angular speed, and nearest-agent distance (Eq. 15), which is reasonable but non-standard. Reporting the standard WOSAC realism meta-metrics on the same checkpoints would make the realism claim more comparable to prior work.
  • Missing comparison with an in-training alternative. A natural non-plug-and-play counterpart is to train the base simulator from scratch with the same handcrafted criteria as auxiliary losses or reward terms. Without this comparison it is hard to judge whether CRAFT's post-hoc approach is uniquely beneficial, or whether the signal is simply valuable in any form.
Questions for authors
  • If the base simulator is trained from scratch with the auto-labeler criteria as an auxiliary loss (not post-hoc), how does the result compare to CRAFT? This is the natural "in-training" counterpart.
  • Why does cross-simulator transfer to RLFTSim yield only +2.73 compared to +6.03 for SMART? Is RLFTSim's distribution closer to CAT-K's (the training source) or further?
  • Does CRAFT help on rare scenarios specifically, or does the improvement come from suppressing minor violations across many ordinary scenarios? A breakdown by scenario type would be informative.
  • Does extending to two- or three-step lookahead improve closed-loop score, and if so at what compute cost?

Minor issues

  • Figure 2's y-axis label "event rate" conflates three metrics (collision, offroad, traffic-violation) at different scales. Please split or clarify.
  • Table 1: "Spd/Ang/Dist" JSD numbers would benefit from a baseline log-replay reference (which is reported as 0.00) directly in the realism-score column.
5 comments

Thank you for the careful review and constructive suggestions. We have submitted the revised manuscript, with changes highlighted in blue. And we respond to your concerns below.

W1. The auto-labeler is doing much of the work. Table 1 shows that CAT-K + "Auto-labeler" already achieves closed-loop good score 75.83 vs. 76.10 for Top-K; CRAFT then adds ~6 points to 82.00. This is a real improvement, but the paper should distinguish more clearly between (a) the signal in the handcrafted criteria and (b) the learned CPE's ability to generalize beyond them. Table 2 has this comparison (AL rank 78.33 vs. CRAFT 82.00) but it should be highlighted earlier.

R1. Our learned CPE provides more effective online guidance than directly applying the handcrafted criteria. Its advantage lies in continuous contextual evaluation and action correction during generation.

(1) Continuous, differentiable contextual evaluation. CPE learns a continuous, differentiable scoring function as shown in Fig. 7(a). This feedback allows CRAFT to adjust action probabilities, helping avoid contextually inappropriate outcomes.

(2) Comparable offline selection and stronger online correction. As shown below, offline CPE ranking performs comparably to the auto-labeler (78.33 vs 78.07), with both improving the baseline by approximately 2 points. Using CPE for online guidance increases the score by approximately 6 points (75.83 vs 82.00), whereas direct online auto-labeler guidance does not improve the baseline.

Method on CAT-KClosed-loop score ↑
Top-K, without guidance76.10
Offline auto-labeler ranking78.33
Offline CPE ranking78.07
Online auto-labeler guidance75.83
Online CPE guidance (CRAFT)82.00

(3) Revised presentation. Following your suggestion, we have consolidated these comparisons in Table 2 and moved it earlier to §5.3, after the CPE ablation, to make the contributions of learned evaluation and online guidance explicit.

W2/Q2. The paper does not characterize when transfer succeeds or fails, which would be useful for practitioners deciding whether to adopt CRAFT for their simulator. Why does cross-simulator transfer to RLFTSim yield only +2.73 compared to +6.03 for SMART? Is RLFTSim's distribution closer to CAT-K's (the training source) or further?

R2. All three simulators are affected by L2G context mismatch, but RLFTSim has already mitigated some unreasonable scene behavior through reinforcement learning. Specifically, RLFTSim optimizes collision and offroad rates, resulting in lower baseline rates than SMART and CAT-K and less room for further improvement in these two metrics. CRAFT therefore achieves smaller additional reductions on RLFTSim, contributing to its lower overall score gain. Nevertheless, the same CAT-K-trained CPE further improves all three event rates without adaptation, showing that contextual correction complements RL-based behavioral optimization.

W3./Q4. Does extending to two- or three-step lookahead improve closed-loop score, and if so at what compute cost?

R3. Following your suggestion, we compare one-, two-, and three-step lookahead with the candidate chunk size fixed at 4.

Lookahead stepsCollision (%) ↓Offroad (%) ↓Traffic violations (%) ↓Closed-loop score ↑Full step (ms) ↓
110.8016.6026.6082.00131.166
210.1015.5026.8082.53213.775
39.8016.2026.1082.63297.007

Deeper lookahead substantially increases runtime but provides only marginal additional gains. Three-step lookahead takes 2.26 times the runtime for a 0.63-point score gain. Under a fixed sampling budget, extending the horizon still examines only a small subset of possible future interactions; it does not exhaustively resolve multi-step consequences. The measured benefit therefore supports one-step lookahead as our practical default.

W4. Realism metric choice. The paper reports realism as a mean JSD over speed, angular speed, and nearest-agent distance (Eq. 15), which is reasonable but non-standard. Reporting the standard WOSAC realism meta-metrics on the same checkpoints would make the realism claim more comparable to prior work.

R4. Table 9 in Appendix D.4 reports the complete WOSAC results for the same base simulators and guided models, including the composite score, kinematic, interactive, and map-based terms, event rates, ADE, and minADE.

We use aggregate JSD as the primary motion-realism measure because WOSAC only scores a small designated subset—the ego vehicle and WOMD prediction targets, with up to eight prediction targets—within a scene containing tens to hundreds of agents. Behaviors of the remaining agents are not directly scored. Our Realism score pools speed, angular speed, and nearest-agent distance across all valid moving agents, providing broader coverage of the scene realism. Appendix D.1 illustrates the distinction, and Appendix D.2 reports the modest association between WOSAC score and reasonable rollout rate (ρ=0.286\rho=0.286).

At the default guidance scale, CAT-K's likelihood-based WOSAC scores for designated agents decrease (Table 9), whereas our Realism score performance improved from 1.50 to 1.27 (Table 1), supporting improved scene-wide behavioral rationality and aggregate motion realism.

W5/Q1. If the base simulator is trained from scratch with the auto-labeler criteria as an auxiliary loss (not post-hoc), how does the result compare to CRAFT? This is the natural "in-training" counterpart.

R5. Training-time rule optimization is useful, but does not replace correction against the current simulated context.

(1) The data-level L2G gap remains. An auxiliary rule loss does not restore the interaction context missing from partially observed training logs. For example, a logged yield may depend on an unobserved agent; an auxiliary loss does not reveal that agent or explain when the yield is warranted. It therefore cannot resolve this information gap simply by adding behavioral penalties.

(2) Similar signals help during RL training, but the gains are unbalanced. Table 1 includes RLFTSim, which uses reinforcement learning to optimize similar collision and offroad criteria. Relative to CAT-K, it achieves lower collision and offroad rates, but traffic violations increase from 36.50% to 46.30%. Its closed-loop score is consequently only 0.50 points higher.

(3) CRAFT uses contextual feedback to improve all three event rates together. This raises CAT-K's score by 5.90 points and further improves the RL-refined RLFTSim by 2.73 points.

Q3. Does CRAFT help on rare scenarios specifically, or does the improvement come from suppressing minor violations across many ordinary scenarios? A breakdown by scenario type would be informative.

R6. CRAFT improves both difficult and well-performing scenes, with the largest absolute gain in the low-scoring subset. We group the 1,000 evaluation scenes by their unguided CAT-K closed-loop score (Fig. 9(a)).

Scene groupCAT-K score rangeScenesCAT-KCRAFTImprovement
Rare<333118.0632.26+14.20
Intermediate33–6622649.4759.00+9.53
Common>6674386.6491.11+4.47
All0–1001,00076.1082.00+5.90

The low-scoring group comprises only 3.10% of the evaluation set, yet benefits substantially from guidance. This shows that the gains are not confined to minor corrections in already strong rollouts.

We also compare map-defined scene types using the closed-loop score. The scores below are computed from the event rates in Fig. 9(b–d), following Eq. (14).

Scene typeCAT-KCRAFTGain (points)
All76.1082.00+5.90
Signalized intersections70.5078.66+8.16
Unsignalized intersections89.3590.37+1.02
Curved road segments82.1785.17+3.00
Long straight road segments84.1788.34+4.17

The closed-loop score improves in every reported scene type, showing that the benefit extends across different environments. Both the score-group and map-type analyses are now included in Fig. 9 and §5.6.

Minor issue. Figure 2's y-axis label "event rate" conflates three metrics (collision, offroad, traffic-violation) at different scales. Please split or clarify. Table 1: "Spd/Ang/Dist" JSD numbers would benefit from a baseline log-replay reference (which is reported as 0.00) directly in the realism-score column.

R7. Thank you for pointing these out. Revised Fig. 2 separates collision, offroad, and traffic-violation rates into labeled panels on a shared percentage scale, with paired Base/CRAFT lines. Table 1 reports 0.00 for log replay in each JSD column and the Realism score, since each logged distribution is compared with itself.

AuthorsOpenReview ↗

Request for Reply

Dear Reviewer jSWN,

Thank you for your review and helpful suggestions. We’d like to highlight four updates in the revised manuscript:

  • The learned evaluator outperforms direct rule scoring for online guidance with the base simulator frozen. We moved this comparison earlier in the manuscript.
  • Deeper lookahead yields modest gains at substantially higher runtime, supporting one-step guidance as the default.
  • CRAFT improves all reported difficulty groups and road types, with the largest gain in the lowest-scoring group.

We would welcome your feedback and would be happy to clarify any remaining points. If the revision addresses your main concerns, we would appreciate your reconsidering your overall rating.

Best regards, Submission25923 Authors

Comments on the paper

2 comments

Dear Reviewers,

The rebuttal deadline is approaching. I am leaving this friendly reminder to encourage active discussion. Thank you for your valuable time and engagement!

AC

AuthorsOpenReview ↗

Summary of the Rebuttal

Dear Reviewers and Area Chair,

We thank you for the time and effort you have devoted to evaluating our submission. We sincerely appreciate your supportive comments highlighting the strengths of our work:

  • Identifying a real and under-discussed problem. Our paper identifies the L2G context mismatch in log-trained traffic simulators and supports it through formal analysis and controlled context experiments. (jSWN, o6LL, w4cx)
  • An effective, simulator-agnostic solution. By decoupling contextual correction from the motion prior, CRAFT enables a single learned evaluator to improve different base simulators without retraining or modifying them, demonstrating strong cross-simulator generality and practical value. (jSWN, o6LL, w4cx)
  • Efficient and effective online guidance. Candidate evaluation takes only 3.97 ms under the profiled configuration, supporting real-time deployment. (jSWN, o6LL)

Building on this positive feedback, we also thank the reviewers for their constructive suggestions, which we have carefully addressed as follows:

Reviewer(s)Main concernResponse and supporting evidence
jSWN, o6LLContribution of learned CPE beyond handcrafted rulesTable 2 shows comparable offline selection performance; learned online guidance improves CAT-K by 5.90 points.
jSWN, o6LLConnection to L2G and benefits beyond training-time optimizationAdded controlled context experiments and demonstrated a further 2.73-point improvement after RL optimization.
jSWN, o6LL, w4cxTransfer across simulators, architectures, and datasetsAdded experiments with GUMP and zero-shot evaluation on Argoverse scenes, supporting transfer beyond SMART and WOMD.
jSWN, w4cxPoor proposal distributions and difficult scenariosAdded scene-level analyses and recovery cases; the lowest-scoring scenes improve by 14.20 points.
jSWN, w4cxMulti-step lookahead, efficiencyDeeper lookahead yields only marginal gains, supporting our one-step strategy as a more practical choice for online guidance.
o6LL, w4cxEvaluation reliability, supervision quality, and sensitivityReported variability, human-evaluation details, training-objective ablations, and inference sensitivity analyses.

We are pleased that our rebuttal has addressed the concerns of Reviewers jSWN and o6LL, and we are particularly encouraged by Reviewer jSWN's decision to raise the score to 3. Although Reviewer w4cx has not yet responded, we believe that the additional experiments and clarifications address his/her main concerns.

Finally, we believe this additional evidence strengthens the case for CRAFT's effectiveness, efficiency, and transferability, and we hope it will support a more favorable assessment of our submission. We will release our code, models, and data to ensure full reproducibility for the community. Through this release, we also hope to inspire further research toward more stable, realistic, and reliable traffic simulation for real-world applications. Thank you again for your thoughtful consideration and for guiding the review process.

Sincerely,

Submission25923 Authors

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

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