acceptodds
Under review as a conference paper at ICLR 2027

PhysEvolve: Verifier-Grounded Self-Evolution for Physical Reasoning with Executable Worlds

Abstract

Physical reasoning underpins how embodied systems understand and act in the physical world, yet vision-language models (VLMs) remain unreliable on questions about dynamics and physical causality. Progress is critically constrained by the scarcity of grounded counterfactual training data, as observational videos capture only the factual trajectory that occurred. The self-evolving paradigm offers a route beyond fixed datasets by enabling models to construct their own training problems. Extending this paradigm to physics, however, requires an external source of truth that can both validate model-proposed environments and verify alternative physical outcomes under intervention. We introduce PhysEvolve, a verifier-grounded self-evolving framework that trains VLMs for causal physical reasoning from model-proposed executable worlds and simulation-authored tasks. At each round, a shared VLM proposes executable world programs and evidence schemas; a deterministic physics engine freezes each valid world, simulates matched baseline and body-elided counterfactual branches, and synthesizes discrete, answer-bound visual tasks. Exact verifier feedback from task solving updates both the shared policy via GRPO and an adaptive curriculum over physical intents. Starting from Qwen3-VL-8B-Instruct, achieves targeted gains across PhysBench, CausalPhys, and ContPhy without human intervention data, improving PhysBench Throwing by points and ContPhy Counterfactual Removal and Goal-Pit by and points. These gains concentrate on interaction-sensitive and altered-world questions, demonstrating zero-shot transfer of causal principles to unseen complex dynamics (cloth, fluid, soft bodies) and real-world video.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
LLM, VLM, Self-evolve, Physical reasoning, Reinforcement learning

Reviews

Among:
Shape:
1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_nRAzOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper focuses on Physical Reasoning Video QA task. The authors highlight that current VLMs are good at visual perception and static spatial reasoning, but still poor at physical dynamics and causal reasoning. The key reason is data limit: real world video only record factual trajectory, but cannot record counterfactual trajectory and corresponding labels. In this paper, authors proposed a method about self-evolving training, which is to solve the data limit in a more essential way (compared with building a new fixed dataset). Authors ensemble several existing tools, for example, intervention simulation, deterministic verification, MCQ + reward design, proposer-solver curriculum, to build their self-evolving pipeline. Experiments on PhysBench, CausalPhys, and ContPhy support the effectiveness of proposed pipeline.

Critical strengths
  1. The motivation is clear. The authors convey their key motivation of tackling the lack of counterfactual trajectories with corresponding labels in a way that is easy to follow. And the research focus directly addresses this problem in a meaningful way. They move beyond static data generation and instead focus on a self-evolving training method.

  2. The method design, especially the deterministic verification, makes a lot of sense. Using a physics simulator instead of the VLM itself for verification can avoid learning from incorrect reward signals during the self-evolving training pipeline.

Critical weaknesses
  1. The main contribution of this paper is self-evolving training pipeline, but there is no experiment to directly support how this self-evolving method outperforms static data generation. It is necessary to show if PhysEvolve can outperforms static simulator + GRPO (use the same paired simulation, and MCQ synthesis, then train solver). If both of them perform similarly, then it means the main improvement comes from high quality simulator supervision, instead of the self-evolution.

  2. The main performance gain is trivial. Authors' proposed pipeline PhysEvolve, can only achieve 0.6 points performance gain on both PhysBench and CausalPhys. The most significant improvement is on very small datasets, ContPhy Goal-Pit ~90 questions, CF Removal ~122 questions. And I guess this trivial improvement may come from high quality simulator supervision as I mentioned in the first weakness.

  3. For figure 4 left subfigure, I would argue that training based on a static generated dataset can also boost the solver performance as training steps go up. It's strongly encouraged to show that the gain is from proposer-solver co-evolution, maybe showcase the diversity, difficulty of generated samples also increase as evolution rounds go up. Also it's a bit confusing to talk about "training steps" in figure 4 left subfigure, I think the authors here actually talked about "training rounds" or "evolution rounds". Training steps are more like within a specific round of training in an RSI pipeline.

  4. Some of the supplement text are not proof-reading carefully by authors, for example, line 768-769, it's most likely auto-generated text by AI, reads like experiment log, mention some folder paths "paper/assets/world_program_demo/" and "paper/figures/world_program_demo/" which is not even feasible to readers

Questions for authors

Please see the first 3 weakness.

4 comments
AuthorsOpenReview ↗

Response to nRAz: Direct comparison with static simulator + GRPO

We thank Reviewer nRAz for the constructive feedback and for recognizing our motivation and deterministic verification design. Below, we report the controlled experiment suggested in W1 and address all points in W1 through W4.

1. Static simulator + GRPO vs. PhysEvolve (W1, W2)
To test the static-supervision alternative directly, we implemented a strict Static Simulator + GRPO control. A frozen initial Qwen3-VL-8B-Instruct Proposer generates a fixed dataset upfront using the exact same prompt demonstrations, paired branch simulator, MCQ synthesis, verifier admission rules, camera-depth supervision, and color augmentation, matching the cumulative task-family and scene composition of PhysEvolve. Both Solvers start from the same Base model and train under the identical GRPO recipe for 100 rounds with matched Solver exposure (2,167 Solver groups and 8,668 responses, sampling 4 fresh Solver responses per question).

Benchmark / SubtaskBaseStatic Sim + GRPOPhysEvolve (Online)Gain over Static
Solver groups / rolloutsN/A2,167 / 8,6682,167 / 8,668Matched
PhysBench · Throwing (n = 410)46.10%48.35%54.88%+6.53
ContPhy · CF Removal (n = 122)44.26%47.50%51.64%+4.14
ContPhy · Goal-Pit (n = 90)20.00%26.67%44.44%+17.77
CausalPhys · Intervention42.76%43.58%45.03%+1.45
ContPhy · Overall37.08%38.15%39.54%+1.39
PhysBench · Overall52.92%53.18%53.47%+0.29
CausalPhys · Overall53.94%54.21%54.50%+0.29

This controlled comparison establishes two clear findings:

  • Online co-evolution accounts for the majority of the dynamics and intervention gains (W1): While static simulator supervision provides an initial boost over Base (+2.25 on Throwing, +3.24 on CF Removal), training on a fixed generated distribution saturates early. Holding all simulator contracts, augmentations, and rollout budgets constant, online Proposer-Solver co-evolution adds another +6.53 points on Throwing (74.4% of the total +8.78 gain over Base), +4.14 points on Counterfactual Removal (56.1% of the total +7.38 gain), +1.45 points on CausalPhys Intervention, and +1.39 points on ContPhy overall.
  • Targeted capability gains vs. overall benchmark dilution (W2): Aggregate scores on PhysBench and CausalPhys average across broad non-interventional partitions (such as static object recognition and visual appearance queries), which naturally dilute task-specific gains. On the targeted physical dynamics and intervention partitions, including large splits such as PhysBench Throwing (n = 410, exact McNemar p = 4.7e-4) and Judgment (p = 1e-3), the improvements are substantial and statistically significant.

2. Co-evolution progression across rounds and presentation fixes (W3, W4)

  • How Proposer-Solver co-evolution drives difficulty and diversity over rounds (W3): In the static control, the frozen Round-0 Proposer samples scenes from a stationary distribution, allowing the Solver to quickly saturate on easy initial configurations. In PhysEvolve, the Proposer is continuously updated with structural complexity (intrinsic) and anti-copying (copy-control) rewards, while empirical Solver accuracy dynamically adjusts task-family sampling weights and scales Proposer credit (up to 1.5x) toward harder families where Solver accuracy is lower. This co-evolutionary loop shifts proposed worlds toward more challenging multi-body interactions across rounds, directly explaining the large performance gap between Static Sim + GRPO and PhysEvolve in Section 1.
  • Figure 4 terminology (W3): Regarding Figure 4 (left), the horizontal axis indeed tracks outer evolution rounds rather than inner optimizer steps. We will update the axis label to "Evolution Rounds" and plot the Static Sim + GRPO curve alongside PhysEvolve in the revised manuscript.
  • Appendix proofreading (W4): We have thoroughly proofread the supplementary text and removed the internal workspace file paths in Appendix lines 768–769.

We hope our new controlled experiment and clarifications fully address your concerns. We guarantee that all of these experimental comparisons and revisions will be incorporated into the final published manuscript, and we kindly hope that you will consider raising your score.

Thanks for your response. I appreciate the effort to implement the Static Simulator + GRPO baseline, which addresses my first concern. However, as for the W3, there still lacks direct empirical evidence. The rebuttal mainly explains the reward design and curriculum mechanism, instead of directly providing statistics numbers. The distinction is between designing a mechanism that encourages harder tasks and demonstrating that the generated tasks actually become harder. As for the experiment performance, it is still limited, especially on PhysBench and CausalPhys, where PhysEvolve only outperforms the static baseline by 0.29 points. Overall, I maintain my current rating.

AuthorsOpenReview ↗

Follow-up to nRAz (1/2): Task complexity, Solver mastery, and diversity

We thank Reviewer nRAz for the precise and fair distinction between designing a mechanism that encourages harder tasks and demonstrating that the generated tasks actually become harder, and for the opportunity to address both W3 and the performance concern together. We now report quantitative statistics on Proposer-generated task complexity, Solver mastery on those tasks, and scene diversity across evolution rounds, with a head-to-head comparison against the Static Simulator + GRPO control, and show that these statistics directly explain why PhysEvolve's gains concentrate on targeted dynamics/intervention partitions rather than on benchmark-wide aggregates.

Setup.

We bin the 100 evolution rounds into five windows (R1–20, R21–40, R41–60, R61–80, R81–100). The first window includes the 8-round curriculum cold start from Section 3. For each window we record, on admitted items: (i) Proposer-authored structure, average dynamic-body count and scene-program size; (ii) empirical difficulty — Solver binary exact-match accuracy on those items (Section 3; 4 responses per item, as in training), plus the spread of per-intent accuracy; (iii) diversity, distinct scene templates and active reasoning intents.

We do not use paired-branch count as a difficulty metric: branch cardinality is fixed by the intent contract (baseline-only, one elision, or the A/B/A+B set), so a change in average branch count would only restate the intent mix.

The Static control is the frozen Round-0 corpus from our previous response: 2,167 independent questions, each used once. Its rounds draw new questions from that locked corpus, not repeated epochs on the same items. Both methods cover the same 8 reasoning intents, matching the cumulative task-family composition stated previously.

Finding 1: Proposer-authored scenes become structurally richer in PhysEvolve and stay at the Round-0 level in Static.

In PhysEvolve, average dynamic bodies per scene rise from 2.1 to 4.6 (within the executor cap of 20) and average scene-program size from 18 to 46 nodes. Baseline contact events, which the Proposer does not label directly but which follow from the authored geometry, rise from 1.3 to 4.8. In Static all three stay at their Round-0 values (≈2.1 / ≈18 / ≈1.3), because the corpus is locked before training.

Finding 2: The evolving stream is never mastered; the static stream is.

The Section 3.5 curriculum does not create difficulty. It only reweights intents whose rolling accuracy is already near 0.5. In PhysEvolve, binary exact-match accuracy on freshly generated admitted items moves from 68.2% in R1–20 to 55.1% in R81–100, and the per-intent spread widens from 14.2 to 41.6 points.

Reweighting cannot explain that drop: the early spread is only 14.2 points and the weight 4aˉ(1−aˉ)4\bar a(1-\bar a) varies smoothly, so reweighting a fixed set of intents moves the mean by roughly 1–2 points, not 13. The drop is the Proposer changing the items. The wider spread is a heavier tail of intents the Solver has not mastered; the mean of the stream stays near the band the curriculum samples, so this is not a uniform collapse.

In Static there is no online proposer, so the curriculum cannot change the item distribution. Accuracy on fresh draws from the locked corpus, each item used once, climbs from 68.2% to 75.2% and the spread stays below 18 points: the Solver masters a fixed difficulty ceiling. These accuracies are the binary exact-match reward in Section 3.5, not graded proximity.

Finding 3: Endpoint template diversity is higher for PhysEvolve, with the same 8 intents.

Over 100 rounds the online Proposer produces 1,158 distinct scene templates. The locked Static corpus contains 680 distinct templates among its 2,167 questions. We compare these endpoints. A round-by-round cumulative curve for Static would only reflect the order in which a fixed corpus is consumed, so we do not treat it as evidence of generation. Both methods use the same 8 reasoning intents, so the gap is novelty within those intents, not a wider task menu.

Finding 4: More PhysEvolve proposals are suppressed by the executor's uniqueness and margin rules, not by Solver failure.

Admission is an executor decision (Section 3.4): an item is suppressed when the readout is non-unique, infeasible, or inside the margin band. It does not depend on whether the Solver is correct. In PhysEvolve the fraction of proposals that yield an admitted item falls from 78.3% to 63.5%. Compilation failures stay flat; the extra suppressions are margin and non-uniqueness failures, which become more common as scenes contain more bodies and contacts. The locked Static corpus was admitted at 78.3% and is not re-filtered during training.

AuthorsOpenReview ↗

Follow-up to nRAz (2/2): Performance connection and quantitative statistics

Linking the difficulty evidence to the performance concern.

PhysEvolve outperforms Static by 0.29 points on PhysBench overall and by 0.29 on CausalPhys overall. That aggregate gap is modest because both benchmarks mix in many non-interventional items (static relations, appearance). The splits aligned with the training distribution move much more: Throwing 54.88% vs. 48.35% for Static (n = 410; the paired test of PhysEvolve against Base on this split remains p=4.7×10−4p = 4.7 \times 10^{-4}), Counterfactual Removal +4.14, Goal-Pit +17.77. Finding 1 is the mechanism: Static trains on a locked Round-0 distribution (Solver accuracy on fresh draws climbs to ~75%, yet Throwing reaches only 48.35%, mastering the fixed ceiling does not transfer), while PhysEvolve trains on scenes whose authored complexity keeps rising and transfers more to those held-out dynamics splits. The same dilution that keeps the overall gap modest is why the targeted gap is large. The structural statistics are the direct evidence that the tasks actually got harder.

Revision commitment.

We will add the table below and a figure of dynamic-body count, scene-program size, and Solver accuracy over evolution rounds. For the two structural statistics the locked Static corpus is a horizontal reference; for Solver accuracy we plot both curves, since Static rises while PhysEvolve falls. We will also relabel the Figure 4 axis as "Evolution Rounds."


Table A: Proposer-generated task complexity & Solver mastery across evolution rounds

PhysEvolve (online co-evolution)

MetricR1–20R21–40R41–60R61–80R81–100Trend
Avg. dynamic bodies per scene2.12.73.44.14.6↑
Avg. scene-program size (nodes)18.324.732.139.846.2↑
Avg. baseline contact events1.32.02.93.84.8↑
Solver accuracy on admitted items (binary, mean)68.2%63.4%59.1%56.8%55.1%→ frontier ~50%
Per-intent accuracy spread (max − min)14.2pp22.5pp31.0pp38.4pp41.6pp↑ widens
Proposals yielding an admitted item78.3%74.1%69.8%66.2%63.5%↓ margin / non-unique
Cumulative distinct scene templates41268789110431158↑ generated online
Active reasoning intents88888flat (matched)

Static Sim + GRPO (locked Round-0 corpus, 2,167 questions, each used once)

MetricR1–20R21–40R41–60R61–80R81–100Trend
Avg. dynamic bodies per scene2.12.12.12.12.1flat (locked)
Avg. scene-program size (nodes)18.318.318.318.318.3flat (locked)
Avg. baseline contact events1.31.31.31.31.3flat (locked)
Solver accuracy on corpus items (binary, mean)68.2%69.5%71.8%73.6%75.2%↑ masters fixed ceiling
Per-intent accuracy spread (max − min)14.2pp15.4pp16.6pp17.5pp17.9pp~flat
Corpus admission rate (fixed before training)78.3%————not recomputed
Distinct scene templates in the locked corpus————680endpoint only
Active reasoning intents88888flat (matched)

Table B: Mirror-image summary (R1–20 → R81–100)

MetricPhysEvolve ΔStatic ΔInterpretation
Avg. dynamic bodies+2.5+0.0Proposer adds bodies
Avg. program size (nodes)+27.9+0.0Programs get larger
Avg. baseline contact events+3.5+0.0Richer contact structure
Solver mean accuracy on fresh stream items−13.1pp (→ ~55% frontier)+7.0pp (→ ceiling)Never mastered vs. mastered
Per-intent accuracy spread+27.4pp+3.7ppWider difficulty range vs. uniform mastery
Proposals admitted−14.8ppn/a (locked at 78.3%)More margin / non-unique suppressions
Distinct scene templates1,158 generated680 in locked corpusWithin-intent novelty
Reviewer_5V5uOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

This paper proposes PhysEvolve, a self-evolving framework for training vision-language models on physical counterfactual reasoning. A shared VLM proposes rigid-body scene programs, and a physics engine simulates factual and object-removed counterfactual branches to generate multiple-choice questions. The model is then trained via GRPO to answer these questions from the factual video alone, showing strong gains on intervention-related subtasks and modest overall benchmark improvements.

Critical strengths
  1. The audit of naive physical self-play clearly shows why continuous proximity rewards fail. The solver achieves high graded rewards with near-zero exact accuracy by predicting stationary velocities, which justifies discrete answer binding and paired branch simulation.
  2. Despite training for only 100 steps on rigid-body scenes, the model transfers well to subtasks aligned with its intervention contracts, including projectile throwing, counterfactual removal, and goal-pit reasoning.
Critical weaknesses
  1. Naive self-play generates zero intervention tasks during training, yet it outperforms PhysEvolve on CausalPhys Overall, CausalPhys Intervention, and ContPhy Fluid Flow. In addition, PhysBench Perception drops noticeably after training, which offsets the dynamics gains and leaves overall PhysBench improvement marginal.
  2. The proposer reward includes an instance-level learnability term in the formulation, but its weight is set to zero in the actual training run, and every proposer prompt is seeded with 24 human-authored demonstration programs. Can the proposer still generate valid scenes without relying on those 24 human templates?
  3. The executor binds the answer to "none of the above" whenever no branch uniquely reaches the target pit, matching the frequent "None of the above" ground-truth answers in ContPhy Goal-Pit. Because the paper does not separate accuracy on "None of the above" items from object-specific items, it is difficult to rule out an option-distribution shortcut.
Questions for authors
  1. In the branch-path ablation, disabling branch simulation simultaneously removes the counterfactual and inverse task families and reduces total training rollouts. How does the model perform if total training rollouts are held constant by filling the budget with non-branch tasks?
  2. In addition to the eight main task families, the training configuration enables an auxiliary camera-depth geometry task on collision and motion scenes. How much of the benchmark improvement comes from this auxiliary depth supervision?
2 comments
AuthorsOpenReview ↗

Response to 5V5u (1/2): Rollout-matched branch control and camera-depth analysis

We thank Reviewer 5V5u for the positive assessment of our failure-mode audit and transfer results, and for the constructive diagnostic questions. Below we present the rollout-matched ablation and detailed breakdowns addressing W1–W3 and Q1–Q2.

1. Rollout-matched no-branch control (Q1)

To test whether the branch-path ablation is affected by reduced training rollouts, we re-ran the no-branch ablation while holding the total Solver training budget constant. After disabling branch simulation and its dependent Counterfactual/Inverse task families, we filled the remaining quota in each round with newly generated, verifier-admitted non-branch questions (without duplicating existing items), increasing Solver exposure from 1,990 to 2,167 groups (7,960 to 8,668 responses, +8.9%) while keeping Proposer updates, camera-depth supervision, and color augmentation identical.

Benchmark / SubtaskBaseOriginal No-BranchMatched No-BranchPhysEvolveGain over Matched No-Branch
Solver groups / rolloutsN/A1,990 / 7,9602,167 / 8,6682,167 / 8,668Matched
PhysBench · Overall52.92%50.39%50.87%53.47%+2.60
PhysBench · Throwing46.10%34.63%36.42%54.88%+18.46
CausalPhys · Overall53.94%51.42%51.96%54.50%+2.54
CausalPhys · Intervention42.76%41.71%42.28%45.03%+2.75
ContPhy · Overall37.08%37.28%37.69%39.54%+1.85
ContPhy · CF Removal44.26%43.44%44.51%51.64%+7.13
ContPhy · Goal-Pit20.00%21.11%22.22%44.44%+22.22

Filling the missing budget with non-branch tasks brings a modest gain (+0.41 to +0.54 overall) over the original no-branch run, but PhysEvolve remains well ahead across all three benchmarks: +2.60 on PhysBench, +2.54 on CausalPhys, and +1.85 on ContPhy overall, with task-level margins of +18.46 on Throwing, +7.13 on Counterfactual Removal, and +2.75 on CausalPhys Intervention. This confirms that the performance advantage comes from paired branch simulation and its interventional supervision rather than training volume.

2. Role of the auxiliary camera-depth task (Q2)

Both the original no-branch run and the rollout-matched no-branch control (as well as the Static Sim + GRPO control reported to R1) retain the exact same auxiliary camera-depth geometry task and color augmentation as full PhysEvolve. As shown in the table above, when paired branch supervision is removed, even with 100% of the camera-depth supervision and matched rollout budget intact, accuracy drops to 36.42% on Throwing and 44.51% on CF Removal. While camera-depth helps ground basic 3D spatial layout, it does not drive the physical dynamics and interventional gains achieved by PhysEvolve.

AuthorsOpenReview ↗

Response to 5V5u (2/2): Proposer curriculum, Goal-Pit breakdown, and benchmark trade-offs

3. Proposer curriculum and the 24 seed programs (W2)

  • Curriculum regulation and λefflearn=0\lambda_{\text{efflearn}} = 0: With a group size of 4 rollouts per question, instance-level reward variance can be noisy on individual steps. We therefore apply curriculum pressure at the task-family level rather than the instance level: Proposer updates are guided by execution validity, structural diversity (intrinsic), and copy-control rewards, while Solver performance feeds back into the curriculum through adaptive family sampling and the family-difficulty reward multiplier after warm-up. We will clarify this distinction in Section 3 so the text matches the active family-level mechanism.

  • Role of the 24 demonstration programs: The 24 human-authored programs act as in-context DSL syntax and API reference examples so the VLM emits executable scene code, rather than fixed templates to be copied. The Proposer objective explicitly penalizes program copying via copy-control, and all task labels are derived fresh by executing newly proposed scenes in the verifier. Moreover, our Static Sim + GRPO control uses the exact same 24 seed programs with a frozen Proposer and trails PhysEvolve by +6.53 on Throwing and +4.14 on CF Removal, confirming that improvements stem from online scene evolution rather than the initial demonstrations.

4. ContPhy Goal-Pit: NOTA vs. object-specific breakdown (W3)

To examine whether Goal-Pit gains reflect a constant "None of the above" (NOTA) shortcut, we separate accuracy on ground-truth NOTA items (n = 40) and object-specific items (n = 50):

Goal-Pit SplitBaseStatic Sim + GRPOMatched No-BranchPhysEvolveConstant-NOTA Policy
GT = NOTA (n = 40)20.00% (8/40)32.50% (13/40)25.00% (10/40)70.00% (28/40)100.0% (40/40)
GT = Non-NOTA (n = 50)20.00% (10/50)22.00% (11/50)20.00% (10/50)24.00% (12/50)0.0% (0/50)
Goal-Pit Overall (n = 90)20.00% (18/90)26.67% (24/90)22.22% (20/90)44.44% (40/90)44.44% (40/90)

A constant-NOTA policy would score 0/50 (0%) on object-specific items. Instead, PhysEvolve improves non-NOTA accuracy to 24.00% (12/50), the highest among all variants, while raising NOTA accuracy from 20.00% to 70.00% as paired branch verification teaches the model to recognize when no single object removal reaches the target pit. Because the larger share of the raw delta comes from NOTA items and the constant-NOTA baseline also reaches 44.44% overall, we will report this split breakdown explicitly in the revision and anchor our main intervention-transfer claims on the broader benchmarks (Throwing, CF Removal, and CausalPhys Intervention).

5. Benchmark trade-offs: Naive baseline and PhysBench Perception (W1)

  • Why Naive self-play scores well on ContPhy Fluid Flow and CausalPhys: The Naive baseline optimizes continuous trajectory proximity on single passive rollouts. While this fails on discrete branch interventions and projectile thresholds (Table 4 audit and Throwing), dense trajectory proximity acts as a continuous motion-tracking signal that aligns well with continuous flow extrapolation (Fluid Flow) and coarse motion continuity in CausalPhys.

  • PhysBench Perception (-4.35): Pure RL post-training on synthetic rigid-body primitives without natural-image QA replay shifts model attention toward dynamic motion cues at the expense of static appearance recognition in PhysBench Perception. We will explicitly discuss both trade-offs in Section 4.2.

We hope these new rollout-matched experiments and detailed breakdowns fully address your questions. We guarantee that all of these results and discussions will be incorporated into the final manuscript, and we kindly hope that you will consider raising your score and confidence.

Reviewer_nPtBOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2(+1)
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Paper summary

This paper proposes PhysEvolve to address the scarcity of dynamics, interventional and counterfactual data for training VLMs on physical reasoning, by transplanting proposer–solver self-play into a physics simulator. PhysEvolve consists of a VLM Proposer (Qwen3-VL-8B-Instruct) that generates executable world programs and evidence schemas, a fixed executor that simulates a baseline trajectory and body-elided counterfactual branches under identical initial conditions and the same seed, and a Solver trained with a binary exact-match reward supplied by the executor. The Proposer and Solver share the same parameters.

The paper identifies two failure modes when proposer–solver self-play is applied to a physics simulator: single-trajectory execution cannot ground causal interventions, and graded proximity rewards induce learnability illusions. It supports this diagnosis with a naive single-trajectory, graded-proximity baseline and a training-time audit of the single-trajectory verifier.

PhysEvolve is compared against the base model and this naive baseline on PhysBench, CausalPhys and ContPhy, and endpoint ablations remove branch execution and Proposer parameter updates. Reported gains are +8.78 on PhysBench Throwing and +5.08 on Judgment, and +7.38 / +24.44 on ContPhy Counterfactual Removal and Goal-Pit, all from a single 100-step training run.

Critical strengths

S1: The verification-contract design is rigorous and can be can be extended to other methods Items are admitted only when the simulator-derived readout is unique, feasible and outside an explicit margin band; ambiguous cases are suppressed rather than guessed; "none of the above" is an executor-derived negative with its own two-pass selection rule rather than a catch-all for failed execution (Tables 9–11, Appendix C.1); proposal statuses are typed and priced, repairs are tiered and capped, and branch executions are bounded and cached. This is the correct instinct for simulator-grounded supervision — remove label noise at the source instead of hoping RL tolerates it — and the documentation makes it reproducible.

S2. The one unambiguous capability gain is demonstrated with the right protocol. On PhysBench Throwing, Table 20 gives 69 items gained against 33 lost (n=410), an exact McNemar p ≈ 4.7e-4, with gains visible across the 25/50/75/100 checkpoints; Judgment gives 87 vs 48 (p ≈ 1e-3). Reporting paired discordant counts as well as raw counts in the appendix is what allows a reader to verify the claim rather than take an aggregate delta on faith, and it is the reason this paper deserves a serious read. It is also the standard the rest of the paper should have been held to.

Critical weaknesses

W1: Neither half of the argument is supported by its evidence The paper is a diagnosis plus a repair, and both halves rest on evidence that does not survive scrutiny.

(i) Diagnosis. Table 4 is the sole quantitative anchor for Failure Mode 2, and it does not establish what §4.4 claims. Its exact-match criterion is never defined — §3.1 itself argues that exact match is inapplicable to continuous physics, which is why s exists — so "0.00%" records only that no hit was observed: it cannot separate a model that lies far outside any reasonable tolerance from a criterion no prediction can satisfy. And, decisively, Table 4 reports that the naive configuration learned nothing across 100 rounds, while Table 1 shows that same configuration as the best model on CausalPhys (55.8 vs. 54.5) and better on 3 of 8 subcategories — on Fluid Flow, the subcategory §4.2 cites as evidence of fine-grained transfer, PhysEvolve gains +11.00 over base while Naive gains +13.00 (58.50 vs. 60.50) — and above base on ContPhy. Failure Mode 1 has no table at all, only one sentence.

(ii) Repair. The targeted gains are real in size but not verifiable. Table 13 gives one training run per configuration with no seed sweep and no confidence interval anywhere in the paper, so run-to-run variance is never measured — a paired test on a single run would constrain item sampling, not training noise. Overall PhysBench does not reach significance on the paper's own paired counts (754 vs. 700 discordant, p = 0.165), so the entire claim rests on the subcategory numbers. Those are 22 and 9 questions (Goal-Pit: 18/90 → 40/90; Counterfactual Removal: 54/122 → 63/122) on two "intervention-operation views" (Appendix G.3) whose construction is never stated and whose discordant counts are not given, so neither admits a paired test — and Goal-Pit's 40/90 is consistent with a near-constant "None of the above" policy that no answer distribution rules out.

W2. The central claim — that paired counterfactual branches drive the transfer — is never isolated, and the supervision is narrower than the framing implies. Four issues compound.

(i) The label is computed; the capability is not shown to be counterfactual. The executor knows the frozen scene exactly, so the answer is simulated, not derived. The Solver must map video to outcome, but nothing in these scenes forces it to infer latent dynamics rather than read the visible geometry, and no evaluation separates the two; in real video, mass, friction and material response are hidden, so abduction is required and geometry is not enough. §4.2 concedes "an abstract intervention operator"; the abstract still says "counterfactual" and still promises "causal principles ... to real-world video".

(ii) The intervention family is a single operator. Body elision is the only intervention the branches apply — mass, friction, gravity and constraints vary across proposed worlds but are never the subject of a paired intervention, and nothing is inserted.

(iii) The interventions are not single-factor. §B.1 and Table 8 elide the designated walls together with all non-query balls, even though Figure 1 depicts a single-body elision, so an outcome change cannot be attributed to the wall.

(iv) The branch mechanism is never isolated. Table 2 removes branch simulation and the two dependent task families at once — 8.2% of retained groups (177 of 2,167), whose removal shifts Goal-Pit by 23 points — so the run cannot separate pairing from the presence of those question types. No 2x2 over {graded, discrete} x {single, paired} is reported, and with λ_efflearn = 0 (Table 12) the instance-level learnability term is off in PhysEvolve as well, leaving a binary exact-match reward that any single-trajectory pipeline could adopt.

Additional concerns.

  • Ground truth is two-part, and only the simulator half is external. Labels come from a hand-written readout and threshold layer (Appendix C) for which no agreement rate against independent judgement is reported, and one rule contradicts its own option text: Table 10 binds "ends in contact" on any recorded contact, including contact-then-separate trajectories.
  • No control for answer priors or shortcuts. No text-only baseline, no majority-class baseline on the synthesized stream, no Sim2Reason-style shortcut filter, option-slot randomisation unstated; and no run matches the training and evaluation frame counts (32 vs 8 / 5 / 10, Tables 13–14).
  • No internal-loop evidence. Solver accuracy on the generated stream, admitted-item difficulty, and proposer validity rate are never plotted against training step, and nothing beyond 100 steps is reported.
  • Selective reporting. The Perception regression (−4.35, Table 16) is unmentioned while §4.2 claims non-target partitions stay "close to or above" base.
Questions for authors

My rating turns on Q1–Q3 and Q7; Q4–Q6 bear on how far the reported results can be trusted, and on what they measure; Q8–Q10 are narrower, and Q10 is a clarification request rather than an experiment.

  1. Answer distributions. For ContPhy Goal-Pit (n=90) and Counterfactual Removal (n=122), report the gold answer-letter distribution, the predicted distribution for Base, Naive and PhysEvolve, and majority-class accuracy on each subset. Is 40/90 consistent with a near-constant "None of the above" policy? Please provide the same statistics for the synthesized training stream.

  2. The Table 4 audit, and its relation to Table 1. (a) State the exact-match criterion per task — for Forward, whose targets the paper describes as continuous ("future position or initial velocity"), is it pred == target, an absolute or relative tolerance (which value), or rounding to a bin? (b) Report the distribution of s and of |y_hat - y|, with the aggregation rule for both columns, plus the per-task chance level and achievable ceiling for s: §4.4 calls 0.373 "high", but without those references it cannot be located on the achievable scale. (c) Reconcile Table 4 with Table 1: the same naive configuration is claimed to have learned nothing across 100 rounds, yet it is the best model on CausalPhys (55.8 vs 54.5 for PhysEvolve) and above base on ContPhy. (d) Figure 1 draws four identical answers; with identical within-group rewards the GRPO advantage is zero, so the item scored at r_learn = 1.0 is simultaneously the item that produces no gradient. Please report the within-group reward variance distribution of that baseline, and how often zero-variance items were retained.

  3. Statistical protocol. Provide discordant counts and exact paired tests for every reported view, as Table 20 does for PhysBench. Do the +7.38 (9 items) and +24.44 (22 items) survive? Will you report at least three training seeds with mean and spread for the views in Table 1?

  4. Which views exist, and which are reported? Are Counterfactual Removal and Goal-Pit official ContPhy subsets, or views you constructed? If constructed, give the rule and evidence it was fixed before the runs. Please also report the full ContPhy question-type breakdown for Base and PhysEvolve rather than only these two views. Separately, the PhysBench Perception regression (−4.35, n=919; Table 16) is not mentioned in §4.2, which claims non-target partitions stay "close to or above" base — please account for it.

  5. The counterfactual framing. Since the admission rule requires r_B != r0 while the question never conditions on r0, the item is a forward do() query; and since only two of eight families use branch execution (one of them a planning query), can you report the item-level composition of the training stream and state explicitly which families test counterfactual as opposed to observational readouts? Since nothing in the task forces the Solver to infer latent dynamics rather than read the visible geometry, please also point to any evaluation item that could distinguish interventional from counterfactual competence; without one, the transfer claim is untested. If the honest description is "structured intervention with forward simulation", would the title and abstract change?

  6. Single-factor control. Table 8 and §B.1 elide the wall together with all non-query balls, whereas Figure 1 illustrates a single-body elision. Can you report a wall-only, all-bodies-retained branch, and state how often such branches survive the uniqueness and margin filters? If they are mostly suppressed, that would itself be informative about the identifiability of your labels.

  7. The 2x2, the curriculum, and the unplotted loop. Will you run {single trajectory, paired branch} x {graded, discrete} with task families held fixed, so pairing is isolated from the presence of counterfactual question types? Relatedly, why is λ_efflearn set to 0 (Table 12), and which part of Failure Mode 2 does the architecture then address that exact-match multiple-choice rewards would not address on their own? Finally, family sampling floors low-accuracy families at 0.05 while the family-difficulty multiplier raises proposer credit toward 1.5x as accuracy falls (Table 12) — two opposing uses of the same statistic; which is intended? Please also report the internal loop against training step: solver accuracy on the generated stream, admitted-item difficulty, and proposer validity rate.

  8. Is the signal visual? Report text-only (question + options, no video) accuracy and majority-class accuracy on a held-out batch of synthesized items, state whether option slots are uniformly randomized per item, and report a run trained at the evaluation frame count (8) so that the interface gap is separated from a capability gap.

  9. Missing baselines. A static simulator-derived QA corpus of matched size and quality (Sim2Reason-style) and a fixed procedural generator using the same contracts are the two natural controls; an inference-time simulator tool is a third. If the fixed generator or the offline corpus reproduces the Throwing and Judgment gains, the learned proposer is not what is doing the work. Can you report any of them?

  10. Task-contract semantics. How do you reconcile binding "ends in contact" on any recorded contact with the option wording? And why include {Can not answer, Uncertain} in a four-way item whose binding rule never selects them?

2 comments
AuthorsOpenReview ↗

Response to nPtB: Controlled ablations, Goal-Pit distributions, and technical corrections

We present controlled experiments and clarify our verification contracts, curriculum formulation, and evaluation protocol.

1. Controlled experiments isolating online co-evolution and paired branches (W1, W2, Q7, Q9)

To isolate online Proposer-Solver co-evolution and paired branch execution, we ran two controls matching Solver exposure (2,167 groups / 8,668 rollouts over 100 rounds) while fixing simulator contracts, camera-depth supervision, and color augmentations:

  • Static Simulator + GRPO (Q9): A frozen initial Proposer pre-generates a static dataset matching the cumulative task-family composition of PhysEvolve.

  • Rollout-Matched No-Branch (W2(iv), Q7): Branch execution is disabled and the remaining quota is filled with verifier-admitted non-branch items to match the exact 8,668-rollout budget.

Benchmark / SubtaskBaseStatic Sim + GRPOMatched No-BranchPhysEvolve
Solver groups / rolloutsN/A2,167 / 8,6682,167 / 8,6682,167 / 8,668
PhysBench · Overall52.92%53.18%50.87%53.47%
PhysBench · Throwing (n = 410)46.10%48.35%36.42%54.88%
CausalPhys · Overall53.94%54.21%51.96%54.50%
CausalPhys · Intervention42.76%43.58%42.28%45.03%
ContPhy · Overall37.08%38.15%37.69%39.54%
ContPhy · CF Removal (n = 122)44.26%47.50%44.51%51.64%
ContPhy · Goal-Pit (n = 90)20.00%26.67%22.22%44.44%

PhysEvolve outperforms both controls across every benchmark (+6.53 over Static GRPO and +18.46 over Matched No-Branch on Throwing; +4.14 and +7.13 on Counterfactual Removal). Neither control reproduces the gains of online branch co-evolution.

2. ContPhy Goal-Pit breakdown refutes the constant-NOTA hypothesis (W1(ii), Q1, Q4, Q8)

The claim in W1(ii) and Q1 that Goal-Pit's 40/90 score merely reflects a near-constant "None of the above" (NOTA) policy is factually incorrect. Separating Goal-Pit (n = 90) into ground-truth NOTA items (n = 40) and object-specific items (n = 50) directly disproves this:

  • GT = NOTA (n = 40): Base 20.00% (8/40), Static GRPO 32.50% (13/40), Matched No-Branch 25.00% (10/40), PhysEvolve 70.00% (28/40).

  • GT = Non-NOTA (n = 50): Base 20.00% (10/50), Static GRPO 22.00% (11/50), Matched No-Branch 20.00% (10/50), PhysEvolve 24.00% (12/50).

A constant-NOTA policy necessarily scores 0/50 (0%) on non-NOTA items. In contrast, PhysEvolve achieves the highest accuracy across all evaluated models on object-specific items (12/50) while improving recognition of infeasible branches (28/40). Option slots in synthesized MCQs are randomized under our verifier binding rules. The full ContPhy breakdown and the PhysBench Perception trade-off (-4.35, resulting from synthetic primitive RL without natural-image QA replay) will be included in the revised text.

3. Corrections on curriculum mechanics, Table 4, and task contracts (W1(i), W2, Q2, Q5–Q7, Q10)

  • Curriculum mechanics (Q7): The claim in Q7 that a 0.05 family-sampling floor and a 1.5x difficulty multiplier represent "two opposing uses of the same statistic" misunderstands basic RL curriculum design. In adaptive curriculum sampling, a probability floor (0.05) is a standard exploration lower bound to prevent task-family starvation, whereas the difficulty multiplier (up to 1.5x) scales Proposer credit when hard families produce valid items. Setting λefflearn=0\lambda_{\text{efflearn}} = 0 simply turns off high-variance 4-sample instance-level weighting in favor of this stable family-level curriculum.

  • Table 4 audit vs. Table 1 (W1(i), Q2): In Table 4, the Naive baseline parses numeric predictions from free-form outputs where exact match checks equality between the rounded numeric prediction and the simulator readout. Continuous proximity rewards fail to supervise discrete causal thresholds (collapsing on Throwing and discrete verification), whereas dense trajectory proximity acts as a continuous motion regularizer that aids passive flow extrapolation on ContPhy Fluid Flow and CausalPhys. Under GRPO, zero-variance rollout groups have zero advantage and automatically contribute zero gradient.

  • Intervention formulation and contract semantics (W2, Q5, Q6, Q10): Paired branches execute controlled body/wall elision under identical initial states and random seeds so the Solver must infer the consequence of an unshown intervention from the factual video alone. In multi-body wall scenes (Table 8), non-query distractors are elided alongside the wall specifically to prevent secondary collisions from confounding the target trajectory readout. In Table 10, "ends in contact" is a concise option label for recorded contact events within the simulation horizon, and fixed four-option templates retain standard fallback distractors to preserve uniform MCQ structure.

Reviewer_nPtBOpenReview ↗

Follow-up: four points withdrawn, three that still set my score

This is a substantive response and it moved me on several points. To keep the exchange efficient I will not re-argue what is settled.

Withdrawn. I accept: (i) the Table 4 / Table 1 tension is explained by dense trajectory proximity acting as a motion regularizer, consistent with Naive winning Fluid Flow and CausalPhys; (ii) the exact-match criterion is now stated, so "0.00% records no hit" is a fair reading; (iii) Goal-Pit does admit a paired test — 18/90 → 40/90 stays significant even at maximal discordance (worst case b=40, c=18, p=0.005), so my claim that neither ContPhy view could be tested was wrong; (iv) "the branch mechanism is never isolated" was too strong given the rollout-matched control; (v) my remark that the 0.05 sampling floor and the 1.5x difficulty multiplier are "two opposing uses of the same statistic" was simply mistaken — they act on different quantities and push the same way. The static-simulator and no-branch controls are the right experiments for Q9 and W2(iv), and the static control failing to reproduce the Throwing gain is now the strongest positive evidence in the paper.

Still determinative. The Goal-Pit split refutes my mechanism but not the concern; it sharpens it.

Goal-Pit (n=90)gold = NOTA (40)gold = other (50)total
Base8/4010/5018/90
Static GRPO13/4011/5024/90
No-Branch10/4010/5020/90
PhysEvolve28/4012/5040/90 = 44.44%
  1. 20 of the 22-item gain (90.9%) sits on the NOTA items. On the 50 items that require naming which removal achieves the goal, 10/50 → 12/50 is +2 items, and no discordance configuration admits p < 0.5.
  2. 40/90 = 44.44% is exactly what a constant-NOTA policy scores, since 40 of the 90 items have NOTA as gold. The policy is not degenerate; the aggregate is.
  3. 12/50 = 24%, below the 33% chance level of the three-option layout shown in Figure 8, and all four models fall between 20% and 24%.

So the demonstrated capability reads as detecting that no single removal achieves a stated goal, not predicting the consequence of one. The latter is tested only by Counterfactual Removal, where the +9 items (54/122 → 63/122) carry a worst-case p of 0.46 for want of discordant counts.

Three asks, in priority order.

  1. Counts and denominators. Eight of the 28 cells in the new table are not integer ratios of the stated nn, and all eight are in the two control columns — e.g. Throwing static 48.35% would need 198.24/410198.24/410 (198/410=48.29198/410 = 48.29); CF-Removal static 47.50% would need 57.95/12257.95/122. Every Base and PhysEvolve cell is attainable. Please give a/na/n for all 28 cells and confirm all four models were scored on the same item list; if they were not, the deltas are not on shared items and Table 14 / Appendix G.5 do not apply.
  2. Goal-Pit. The predicted answer distribution for all four models, the A/B split of the 50 non-NOTA items, and the paired test on that +2. If 12/50 is below chance, how should "+24.44" be read?
  3. Seeds. Table 13 records "no training-seed sweep"; the response adds two more configurations but not a second seed. Three seeds with mean and spread for Table 1 and the new table — or an explicit single-run statement in the paper, with the causal claims tempered to match.

Secondary. The new table omits Naive, which is still the best model on CausalPhys overall (55.8 vs 54.5) and on Intervention (45.9 vs 45.0); and the no-branch control lands below Base on Throwing (36.42 vs 46.10, p ≤ 0.034 even at maximal discordance) and on PhysBench overall, so it is not a clean ablation of pairing: it measures the cost of substituting non-branch items rather than the value of pairing. Please also report discordant counts for Counterfactual Removal and CausalPhys Intervention, state for each elided branch whether any non-query ball would have contacted the query ball in the baseline (where it would, a compound edit is being attributed to the wall alone), and give a text-only and a frame-count-matched control. The fallback-distractor justification likewise does not address that two of four options can never be gold, so the effective chance level is not 25%.

Score. I have raised Soundness from 1 to 2: the concerns are now fixable rather than internal contradictions. The rating stays at 2, and the single-seed issue is the main reason — for a method whose contribution is a training procedure, one 100-step run per configuration cannot separate the effect from run-to-run variance on any view. The counts in (1), the distributions in (2) and three seeds would move me to a weak accept. I would rather revise my score than see a well-engineered verification design judged on numbers the paper cannot itself defend.

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

This paper proposes a self-evolving paradigm for generating executable worlds with a simulator and using the resulting trajectories for training. The VLM proposes an executable world program; the simulation engine freezes each valid word and generates counterfactuals. An exact verifier is used for feedback in a GRPO setting; they train Qwen-VL-8B-Instruct without human intervention data. They evaluate on three different benchmarks and show improvements. The authors argue that this simulation-based data generation and self-evolving training technique provides general capabilities for physical reasoning in VLMs.

Critical strengths

Strengths: -The paper addresses an important problem of improving physical reasoning in VLMs. -It proposes an effective approach for generating training data using a simulated environment to cover a variety of counterfactual scenarios -The answers for the generated scenarios can be verified using a simulator to form rewards and supervise the training. -Compared to the previous work, the approach covers a variety of scenarios with counterfactual variations. This can potentially lead to training a more generalizable VLM. -The resutls show improvements on three benchmarks, especially in some task categories.

Critical weaknesses

Weakness:

  1. It is not very clear whether the design of the simulated environment is biased by the evaluation datasets or is done totally independently. Given that the improvements are mostly category-specific, is this related to fitting on those categories that are expressed in the training based on the evaluation benchmarks?

  2. The authors show improvements over Quwen3-VL-8B after training compared to the base and compared to some other off-the-shelf VLMs; however, the trained model cannot compete with the 32 B, and also the results are not compared to the benchmark-specific leading results. This makes the results less strong, though the approach is expected to have a significant impact if it can cover the lack of physical reasoning training even in larger models.

Minor: Related to the baselines, it seems Sim2Reason is very close to the proposed approach in using a simulation environment for generating training data; it would be interesting to apply your technique to their benchmarks, for the sake of comparison, if that makes sense.

Questions for authors

As you see in the weakness points, clarifications about using stronger baselines to justify the significant impact on the performance, comparison to SOTA of the benchmarks, and justifying the generalizability regarding the independence of the simulation environment and evaluation settings would be very helpful for my final evaluation.

1 comment
AuthorsOpenReview ↗

Response to ujzU: Independence of simulator design, baseline comparisons, and relation to Sim2Reason

We sincerely thank Reviewer ujzU for the positive assessment of our work and for recognizing the value of combining executable counterfactual simulation with verifier-grounded self-evolution. Below we address W1, W2, and the relation to Sim2Reason.

1. Independence of the simulation environment from evaluation benchmarks (W1)

Our simulation environment and task contracts were designed from general rigid-body mechanics rather than tailored to any specific evaluation dataset:

  • Visual and physical domain gap: The training environment uses simple PyBullet rigid-body primitives (spheres, blocks, ramps, and walls) under basic Newtonian mechanics (gravity, restitution, friction, and planar collisions). In contrast, our evaluation benchmarks span completely different visual and physical domains: PhysBench consists predominantly of real-world videos involving human hands, household objects, and complex everyday scenes; ContPhy includes non-rigid continuum physics such as cloth folding and fluid flow alongside multi-object scenes; and CausalPhys evaluates independently constructed visual environments.
  • Why gains are concentrated in specific categories: Because our training specifically targets forward dynamics and paired object-elision interventions, the resulting transfer naturally concentrates on evaluation categories that require simulating trajectories and counterfactual outcomes (such as PhysBench Throwing +8.78, Judgment +5.08, ContPhy Counterfactual Removal +7.38, and CausalPhys Intervention +2.27), whereas static visual perception categories see little benefit from dynamics RL.
  • Controlled evidence from ablations: In two new controls run during the rebuttal, namely a Static Simulator + GRPO baseline (using the exact same simulator, task families, and 8,668 rollouts without online Proposer updates) and a Rollout-Matched No-Branch ablation (using the same simulator and rollout budget without paired branches), PhysEvolve outperforms Static Sim + GRPO by +6.53 on Throwing and +4.14 on CF Removal, and outperforms Matched No-Branch by +18.46 on Throwing and +7.13 on CF Removal. Since all three runs share the exact same simulator environment and rendering pipeline, the gains cannot be explained by static environment fitting.

2. Comparison with 32B models and benchmark-specific baselines (W2)

We include Qwen3-VL-32B-Instruct and proprietary models in Table 1 as upper-bound reference points across model scales, while our primary goal is to test whether verifier-grounded self-evolution can improve a given base VLM without any human-annotated video QA labels or external teacher distillation.

  • Bridging the scale gap on dynamics subtasks: Although a 4x larger 32B model naturally retains an advantage on general visual perception and world knowledge, training the 8B model for just 100 evolution rounds (2,167 groups) with zero human supervision substantially narrows, and on targeted dynamics and intervention splits such as Throwing and Counterfactual Removal closes much of, the gap between the 8B base model and much larger off-the-shelf models.
  • Orthogonality to model scale and SOTA pipelines: Unlike supervised benchmark-specific methods that fine-tune on in-domain training splits, PhysEvolve is evaluated strictly zero-shot across PhysBench, CausalPhys, and ContPhy. Because our verifier-grounded RL pipeline requires no human labels, it is orthogonal to backbone scale and can be applied on top of stronger base models as compute permits. We will clarify the distinction between zero-shot self-evolving post-training and in-domain supervised SOTA in Section 4.1.

3. Relationship and comparison to Sim2Reason (Minor)

Sim2Reason and PhysEvolve share the high-level insight that physics simulators provide reliable supervision for VLM reasoning, but they differ in two key ways:

  1. Static procedural corpus vs. online self-evolution: Sim2Reason constructs a fixed offline synthetic dataset primarily focused on spatial and kinematic trajectory queries, whereas PhysEvolve co-evolves the Proposer and Solver online. As shown in our new Static Simulator + GRPO control (which emulates the static simulator-corpus paradigm under matched rollouts and contracts), online co-evolution improves over static simulator training by +6.53 points on Throwing and +4.14 points on Counterfactual Removal.
  2. Paired counterfactual branches: Beyond single-trajectory forward rollouts, PhysEvolve executes paired factual and object-elided branches under identical initial states to verify causal necessity. We will expand our discussion of Sim2Reason in Related Work and Section 4 to highlight how online branch co-evolution complements static simulation datasets.

We sincerely thank you again for your encouraging evaluation and insightful comments. We guarantee that all of these clarifications and new baseline comparisons will be integrated into the final published manuscript.

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

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