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Paper summary
The paper proposes Visual Prompt Engineering (VIPE), a training-free pipeline that modifies task images before passing them to a video generation model. An ideator proposes edits, an image editor generates variants, and an optional filter selects faithful transformations. Experiments cover six visual reasoning task families, compare visual and textual prompting, and investigate test-time budget allocation. The authors attribute the improvements primarily to a preference for realistic visual contexts and argue that abstract benchmarks can underestimate video-model capabilities.
Critical strengths
- The paper identifies a practical and useful dimension of video model behavior. Treating the input image as an optimizable prompt provides a complementary approach to changing textual instructions or repeatedly sampling videos.
- The empirical investigation examines several relevant aspects of visual prompt engineering. The paper studies multiple models on VPCT, extends automated exploration to several reasoning tasks, compares textual and visual variants, and investigates inference-budget allocation.
Critical weaknesses
- Task preservation is not sufficiently established. Appendix E.4 lists edits that selectively emphasize target objects or add pairing cues between matching dots. These transformations can perform part of the reasoning before the video model receives the input. Preserving object counts and positions does not ensure an unchanged reasoning challenge, leaving the contribution of the editor’s own task understanding insufficiently separated.
- The central VPCT comparison changes several factors simultaneously. Appendix C changes the textual constraints, removes buckets from VIPE inputs, and uses different output-extraction procedures for original and edited videos. Consequently, the reported 41.3%→59.3% improvement cannot be cleanly attributed to visual presentation alone. Matched instructions, bucket configurations, and a common evaluator are needed.
- The automated-search results do not establish generalization of the selected prompts. Figure 3 reports the best of 20 variants per task/split and explicitly includes per-instance oracle selection, without a clearly separated selection and test set. The 18,160 generated videos in this experiment derive from only 86 starting images, including just 5–6 examples for several tasks. These results demonstrate promising variants, but not their reliability on unseen instances.
- The test-time efficiency claim is only partially demonstrated end to end. VPCT includes an explicit majority-voting procedure and accounts for editing costs. However, Appendix F substitutes a pass-rate proxy for Maze and RushHour while assuming an aggregation mechanism that is not implemented. The complete cost of ACE exploration and constitution learning is also insufficiently documented.
- The interpretation of improved scores as stronger reasoning is overstated. For example, the RushHour evaluator checks each car’s initial move and subsequently ignores tracking failures for that car. Such scores do not establish complete, valid solution trajectories. The realism experiments also change semantic context and affordances, leaving the causal explanation incomplete. The recommendation to stop evaluating abstract tasks is therefore premature; those tasks remain useful tests of representational robustness.
Questions for authors
- How many evaluated edits introduce target-specific emphasis or solution cues? Do the gains persist when editing is restricted to transformations that neither identify targets nor reveal pairing or solution information?
- What improvement remains on VPCT when original and edited inputs use matched textual instructions, identical bucket treatment, and the same human-validated evaluator?
- Can editing strategies be selected on a development set and then evaluated on substantially larger, unseen instance sets? Please distinguish this performance from retrospective best-of-20 and oracle results.
- How would the system select or aggregate a final solution for Maze and RushHour without access to correctness labels? Does the budget advantage persist after including selection, failed edits, retries, and search costs?
- Do the improvements persist under strict trajectory-validity criteria? Can realism be isolated from changes in object salience, semantic cues, and physical affordances?
- How does the automated input-editing framework relate to Visual Persuasion, which also optimizes visual inputs through generative editing? Its task differs, but discussing this connection would clarify the methodological contribution.
4 comments
Author rebuttal (2/3)
VPCT comparison changing several factors simultaneously
This is a valid point. We are currently working on additional results on the main VPCT version with buckets and matched text instructions, using the same evaluator as for the sketch experiment. Results are forthcoming due to the scale of these experiments (35k videos). We note that the primary motivation for the extended prompt was for better control over video generation, and the bucket removal was to encourage simulating the trajectory rather than any prompt rewriter pre-specifying a target bucket - thus if anything, a bucket removal makes the task harder, not easier.
Generalization of the selected prompts
We conducted additional experiments to measure VIPE transfer on a new held-out set of 50 samples per task and observed significant error reduction (ER), reinforcing the transfer benefit of VIPE. We now added these results as the new App. E5 and reference in Sec. 4.
| Task | Free-form: Original ER | Free-form: Held-out ER | ACE: Original ER | ACE: Held-out ER |
| Mean of top-5 variants | ||||
| Conjunctive Search | 40.4% | 32.8% | 37.7% | 5.8% |
| Sort 3 Numbers | 62.5% | 48.3% | 60.0% | 61.0% |
| Connect the Dots | 3.8% | −0.5% | 5.0% | 0.9% |
| Best variant per sample | ||||
| Conjunctive Search | 72.9% | 68.9% | 80.0% | 52.2% |
| Sort 3 Numbers | 79.2% | 74.4% | 100.0% | 97.6% |
| Connect the Dots | 13.8% | 16.3% | 40.0% | 28.8% |
We also clarify that all existing VPCT and ACE results (Sec. 4 and 6) in the paper already show held-out performance. For existing freeform VIPE results, held-out transfer is also seen when excluding the 2 samples used for brainstorming. Conjunctive search: 12/20 beat baseline, best variant 54% error reduction; Sort: 19/20 beat baseline, best variant 77% error reduction, Connect dots: 5/20 beat baseline, 10% error reduction.
Test-time efficiency / pass-rate proxy / cost
First, we clarify that all test-time efficiency experiments (Sec. 5, Figs. 4–5, App. F) use open-loop freeform VIPE (Sec. 4), which requires zero video generations during ideation and no constitution learning. Its full cost is accounted for in our budget analysis. Second, while we reported Pass@k in App. F as a principled upper-bound estimate (which is reported as such), our deterministic RushHour parser already extracts discrete symbolic move sequences, which we can use for majority voting. Analyzing RushHour data (across 500 bootstraps) confirms the exact same end-to-end scaling trend as VPCT. With V = number of VIPE visual prompts, A = number of video attempts, accuracy improves from 29.1% for a single variant with a single attempt (1V x 1A) to 70.4% when allocating a \32.40) at 63.2% (+7.2 pp). This advantage of scaling variants over repeated attempts holds across all budget tiers (e.g., \25: 59.6% for 1V x 7A → 64.3% for 6V x 1A; \$45: 63.2% for 1V x 10A → 73.1% for 12V x 1A), reaching 79.3% at 21V x 1A and 89.8% at 21V x 10A. We have added this end-to-end majority-voting analysis to App. F.
Author rebuttal (3/3)
Interpretation of improved scores as stronger reasoning
That’s a valid point. We don't intend to claim that the underlying planning or reasoning abilities of models improve, but that video model performance on visual reasoning tasks improves as a result of better scene consistency via VIPE. We have now made these explicit and rephrased statements such as "improves visual reasoning capabilities" to "improves performance on visual reasoning tasks" (in intro, list of contributions, etc.), so we don't imply that the model's underlying reasoning gets better. For existing tasks, we directly follow the respective paper’s evaluation methodology (see response to ozs9 for details).
The recommendation to stop evaluating abstract tasks is premature; those tasks remain useful tests of representational robustness.
We realize that the current recommendation of “stop evaluating video models on abstract, impoverished tasks” misses the mark. We’ve now rephrased Takeaway 5 as follows: “For a representative estimate of performance and robustness, make sure to evaluate video models across a broad spectrum of visual representations (e.g., across both abstract and realistic tasks)”. This recommendation is similar to the history of ImageNet classifiers: originally evaluated on just one setting (IN-val), the community built ImageNet variants to test robustness (IN-Sketch, Stylized-ImageNet, IN-R, IN-D, IN-C). Similarly, VIPE can help to build variants of video model benchmarks - in a scalable fashion.
Q1-Q3:
Kindly see response above.
Q4: For Maze, a VLM scores the generated video with a grid overlay and judges whether the runner reaches the goal without violations. For RushHour, a deterministic parser tracks each car and extracts the move sequence. The benchmark-provided validator then checks whether that sequence is valid. Please also see our response above.
Q5. Can realism be isolated from changes in object salience, semantic cues, and physical affordances?
Realism: Unfortunately, it is not possible to change the degree of realism without changing affordance. However, that doesn’t invalidate the causal interpretation of “if realism is increased, the model’s scene consistency improves”. We now mention this explicitly in Sec. 7 (“realism is not necessarily a binary choice but rather a spectrum; with increased realism object appearance and affordance change as well since it is impossible to vary realism without influencing affordances.”)
Q6. How does the automated input-editing framework relate to Visual Persuasion, which also optimizes visual inputs through generative editing? Its task differs, but discussing this connection would clarify the methodological contribution.
Visual persuasion (https://arxiv.org/pdf/2602.15278) is about convincing agents to buy stuff online through image edits; we now mention (at the end of Sec 2) that VIPE is fully modular and thus other edit methods like Visual Persuasion could be dropped in as the editor.
Thanks again, and kindly let us know if these address your questions.
As promised: update on "fully matched" VPCT comparison
Dear reviewer, as promised here is an update on “The central VPCT comparison changes several factors simultaneously [...] Matched instructions, bucket configurations, and a common evaluator are needed”:
We fully agree that it would be problematic if gains from VIPE could be attributed to these factors (different prompts / different bucket setup / ...) instead of realism. In response to your concern, we conducted an additional “matching-everything-but-realism” experiment, where there is no difference between the VIPE and sketch setups except for realism: identical prompt, identical bucket setup, identical aspect ratio, identical number of samples, identical output-extraction procedure, identical evaluator. A paired two-sided scene-level t-test shows a highly significant effect (p < 0.001) for VIPE over sketch, which means that our key result (realism improves performance) holds up. We’ll be adding this result to the article, thanks for the suggestion.
Author rebuttal (1/3)
Dear reviewer YDQh,
Thank you for your comments and suggestions. We’re happy you found the paper “clear and easy to follow”, “identifying a practical and useful dimension of model behavior”, and that your concerns are either “minor or fixable”. We address your concerns below.
We agree this is an important question, and address it in three ways.
(a) Evidence that VPCT edits do not make the task easier
Author verification. Every single VIPE image from Sec. 3 was checked by the authors to make sure it did not make the problem easier.
An independent model does not find the edited images easier. In App. G/H, we ran the same original and VIPE images through Nano Banana 2 with text output. It is less accurate on VIPE images than on the original sketches (Pass@1 50% vs. 58%). If the editor had leaked solution cues into the images, this model should benefit. It doesn't. So the gain is specific to video models, which fits our realism-bias account rather than task simplification.
Control condition. The unnatural-textures control goes through the same editing pipeline and text prompt but does not improve over baseline. Running images through the editor is therefore not enough to help.
(b) Freeform VIPE is sample-agnostic by construction.
In freeform VIPE (Sec. 4), the ideator writes one style edit instruction tedit and it’s applied to every sample, e.g., "render as an anodized metal puzzle box" for RushHour, "low-contrast arcade pixel texture" for Mazes, “3D render of a marble run toy” for VPCT, “convert into pixelated arcade game sprites” for Sort. Style instructions generally don't encode sample-specific solutions, and the generated variants (illustrated in the appendix) don't show a general tendency to have solved part of the task.
(c) Closed-loop ACE, and some tasks:
We agree with the reviewer that some closed-loop ACE strategies for Conjunctive Search and Connect the Dots (App. E.4) go beyond appearance, especially when the task solution is more tied to visual appearance. We conducted additional reviews on these image edits. None of the images in Sort 3 Numbers task contain additional hints. For Connect the Dots, one edit contained hints (same-colored circle pairs are labeled with matching white numbers). For Conjunctive Search, many variants did highlight the two targets more (changing sizes and textures). We are working on updating the paper to report ACE results for Conjunctive search only on variants that ensure solution-equivalence.
However, generally, great care was taken by the authors (who manually checked more than just spatial layout and object counts) to ensure tasks are not solved by the transformation, as can be clearly seen in the multitude of variants for all other tasks. The general results hold.
We also note that a key goal for this work is to establish an analogy between visual prompt engineering for video models and text prompt engineering for LLMs: both rewrites the problem representation to unlock reasoning rather than adding reasoning capabilities. Our results echo text prompt engineering practices that paraphrase problems to model-familiar phrases [1,2] or languages [3,4]. Consistent with these results, we also show that non-visual, text prompt changes also elicit significant performance differences in video models (Sec. 6), suggesting that models are highly sensitive to input representations.
[1] Gonen et al. Demystifying prompts in language models via perplexity estimation. In Findings of the Association for Computational Linguistics: EMNLP 2023.
[2] Deng et al. Rephrase and respond: Let large language models ask better questions for themselves. In First Conference on Language Modeling (COLM), 2024.
[3] Shi et al. Language models are multilingual chain-of-thought reasoners. ICLR, 2023.
[4] Huang et al. Not all languages are created equal in LLMs: Improving multilingual capability by cross-lingual-thought prompting. In Findings of the Association for Computational Linguistics: EMNLP 2023.