- Rating
- 3(+1)
- Confidence
- 4
- Informativeness
- 3
- Presentation
- 3
- Soundness
- 2
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Paper summary
This paper formulates world editing as modifying an existing executable world while preserving unrelated properties, and organizes edits into four intervention levels: property, entity, dynamics, and system. It introduces IGMWorld and IGMBench, comprising 110 game-modding tasks across Minecraft and Terraria, with executable behavioral checks and separate visual-consistency evaluation. The experiments report decreasing reliability for deeper interventions, predominantly behavioral rather than compilation failures, and a gap between functional correctness and visual integration. The main contribution is a benchmark and an analysis of coding-agent capabilities in game modification.
Critical strengths
- Visual consistency is the most interesting aspect of the evaluation. Separating semantic correctness from compatibility with the host game's art style captures a meaningful requirement beyond functional implementation. The reported differences between functional and visual rankings are worth investigating further.
- The benchmark has practical value for game-development agents. Evaluating modifications through actual game states and interactions, rather than compilation alone, provides a useful test of whether agents implement the requested behavior.
Critical weaknesses
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The connection to world modeling and the novelty beyond agentic game development remain insufficiently established. The current setting primarily evaluates coding agents’ ability to modify game properties, content, and systems through existing code, assets, and modding interfaces, rather than learning or editing an environment model. While the benchmark is valuable for game-development and software-engineering agents, its direct contribution to interactive world models remains motivational rather than empirically demonstrated, even though Section 5 appropriately acknowledges the complementary relationship. Moreover, GameDevBench already evaluates modifications to existing game projects using engine-based tests [1]. The authors therefore need to explain what new capabilities or challenges intervention depth reveals beyond reorganizing familiar game-modification tasks. The distinctive contribution should be established through insights into cross-system coupling, preservation of non-target properties, or visual integration—not through the generation-versus-editing framing alone.
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The experiments do not yet convincingly establish intervention depth as an explanatory axis beyond ordinary task complexity. Figure 2 stratifies tasks by criterion count, but tasks within a bin can still differ in game, task type, API difficulty, and the complexity of individual requirements. The results support an association between the assigned levels and success, but do not clearly identify cross-component coupling as the relevant source of difficulty. A small within-game comparison of tasks with similar requirements but different dependencies would be more informative than simply expanding the benchmark.
[1] Wayne Chi et al. GameDevBench: Evaluating Agentic Capabilities Through Game Development. arXiv:2602.11103, 2026.
Questions for authors
- Is this editing in dynamic? In the static case, what distinguishes the evaluated capability from generating a new world variant from a revised prompt?
- Could you clarify the counting units in Table 2, Figure 2b, and CPR? Are the 1,161 criteria in Table 2 unique criteria that can be reused or combined across tasks, or the sum of all per-task criteria? Under the latter interpretation, the average is approximately 10.55 criteria per task, which seems difficult to reconcile with Figure 2b's quartile bins of ≤13, 14–19, 20–28, and >28.
- How well is preservation tested at L3/L4? Since regression checks are concentrated at L1, please report how many deeper tasks include them and which non-target behaviors they protect.
- Could strict thresholds partly explain the low visual pass rates? Table 18 reports mean balanced accuracy of 0.61. Could a small held-out human evaluation verify the main visual conclusion and model rankings?
- One more thing I'm interested in: Did the authors analyze what drives the visual failures? Could you break down visual performance by asset-creation method, image-generation backend, and whether agents inspected native reference assets?
4 comments
Response to Reviewer yJZE (part 2)
Q1: Is Editing Static or Dynamic?
Edits are static. We were aware that dynamic edits were possible in minecraft and terraria, but deeper changes to world mechanics often require underlying implementation.
Distinction from World Generation. World editing starts from an existing world and applies a targeted intervention. The original world provides a fixed reference for verifying intended changes and preserving non-target properties through paired runtime comparisons (§3.1). This introduces explicit consistency requirements across existing mechanics and systems, which are not necessarily enforced when generating a world variant from a revised prompt.
Q2: Clarification of Criterion Counting
Thank you for pointing out this ambiguity. Table 2 counts 1,161 behavioral criteria (10.55 per task), each with at least one executable check. Each criterion may involve multiple checks, yielding 2,771 executable checks (25.19 per task). Figure 2b uses executable check counts for its quartile bins (≤13, 14–19, 20–28, >28), explaining the apparent discrepancy. CPR is calculated over individual executable checks. We will clarify these counting units in the paper.
| Depth | Tasks | Behavioral criteria | Executable checks |
|---|---|---|---|
| L1 | 27 | 174 | 459 |
| L2 | 29 | 306 | 693 |
| L3 | 27 | 323 | 882 |
| L4 | 27 | 358 | 737 |
| Total | 110 | 1,161 | 2,771 |
Q3: Preservation Coverage at L3/L4
The original 225 regression checks (Appendix Table 7) were derived from task-specific requirements. L1 tasks often specify properties to preserve due to parameter change, while deeper tasks L2-L4 primarily describe new content and mechanics, resulting in fewer explicit preservation requirements and sparse regression coverage.
To improve this, we have expanded preservation testing to all 110 tasks, with 711 paired regression checks across four intervention depth levels. Each check compares properties of existing vanilla content against a mod-free baseline under the same environment, with task-specific exemptions for intended changes. The checks cover items, entities, recipes, loot tables, player statistics, and other game-specific categories.
| Depth | Minecraft | Terraria | Total checks |
|---|---|---|---|
| L1 | 82 | 91 | 173 |
| L2 | 90 | 98 | 188 |
| L3 | 84 | 91 | 175 |
| L4 | 84 | 91 | 175 |
| Total | 340 | 371 | 711 |
Across runs, only one preservation check failed, in a run that already failed its authored requirements. Thus, the expanded checks introduced no additional WSR failures, leaving our reported WSR results unchanged.
Q4: Visual Metric Validation
Following the reviewer's suggestion, we conducted a held-out human study of 112 unseen agent-created textures across L1–L4 and 7 model configurations. Annotators familiar with Minecraft and Terraria evaluated each texture in its game context, spending approximately 30 minutes each. We also collected reasons for negative judgments (Q5). TPIPS rejects more textures than human majority judgments, and adjusting α barely improves agreement. Human–TPIPS model-ranking correlation equals to ρ = 0.36. We will revise the paper to state that visual integration is weak under both human and automatic evaluation.
| Measure | Preliminary (40 textures, 9 annotators) | Held-out (112 textures, 3 annotators) |
|---|---|---|
| Style balanced accuracy (α = 0.15) | 0.60 | 0.49 |
| Semantic balanced accuracy (α = 0.15) | 0.62 | 0.59 |
| Mean balanced accuracy (α = 0.15) | 0.61 | 0.54 |
| Best style accuracy (α) | 0.61 (0.10) | 0.56 (0.05) |
| Best semantic accuracy (α) | 0.65 (0.25) | 0.62 (0.20) |
| Human majority joint pass | 55% | 47% |
| Automated joint TPIPS pass (α = 0.15) | 23% | 26% |
Q5: What Drives Visual Failures?
In our held-out human study (Q4), annotators provided reasons for negative judgments (Annotators could select multiple reasons). Among 181 negative responses, the most common reasons were:
| Human-reported failure reason | % of negative responses |
|---|---|
| Mismatched pixels, shading, or outlines | 65% |
| Unrecognizable content | 43% |
| Inconsistent colors | 39% |
| Broken or unfinished appearance | 22% |
We further analyzed our 1,968 scored custom textures using the paper's visual thresholds (α = 0.15, k = 5).
| Factor | Textures | Joint visual pass rate |
|---|---|---|
| Image-generated | 541 | 18% |
| Code-drawn | 648 | 29% |
| Native assets inspected | 609 | 36% |
| Native assets not inspected | 785 | 21% |
After controlling for model, game, and asset category, neither creation method (p = 0.70) nor reference inspection (p = 0.98) significantly predicts success.
We also identify a concrete stylistic mismatch: image-generated Minecraft item sprites contain a median of approximately 115 colors, compared with 10 in native assets and 9 in code-drawn assets. Generated sprites frequently exhibit smooth gradients and anti-aliased edges that differ from native pixel art (Appendix Figure 7).
Thank you for the detailed responses and additional analyses, particularly the expanded preservation checks and held-out human evaluation. These additions address several of my concerns, and I will raise my overall assessment to 3.
I encourage the authors to incorporate these findings and clarifications into the revised paper. Regarding W2, the additional experiment already provides useful insights. I encourage the authors to build on these encouraging results and explore the question in greater depth, which would further strengthen the paper.
For future work, I would be interested in dynamic world editing and in demonstrating how controlled world variants can support agent adaptation and model training or evaluation.
Thank you
Dear Reviewer yJZE,
Thank you for your feedback and for increasing the rating. We have revised the manuscript. Thank you again for your time!
Response to Reviewer yJZE
We thank the reviewer for the detailed and constructive review.
W1: Connection to World Modeling and Distinction from Game Development
We agree that our current experiments evaluate coding agents editing executable worlds. Applications to learned world models remain future work. IGMWorld provides a framework for constructing controlled world variants with changes to entities, dynamics, and interacting systems. These variants could provide intervention data for future world-model training and evaluation (§5). We also acknowledge that GameDevBench also evaluates modifications to existing game projects using engine-based tests. We will clarify this distinction in the related work.
Evidence of distinctive challenges:
W2: Intervention Depth and Cross-System Coupling
We agree that criterion-count stratification alone cannot establish why deeper edits are harder. We conducted additional analyses. Across 110 tasks, adding intervention level to a regression controlling for game, task genre, and complexity measures improves explained variance (R²: 0.455 → 0.518, p = 0.007). The adjusted L1–L4 success gap remains 29 percentage points (95% CI: 7–56), compared with 48 points before adjustment. Following the reviewer's suggestion, we compared 10 pairs of tasks from the same game and genre, with similar executable-check counts but different runtime dependencies.
For example, in Terraria, a silver-coin sword (23 checks, one runtime dependency) succeeds in 5/7 runs, while a reflecting buckler (24 checks, four dependencies) succeeds in 1/7. The buckler frequently fails projectile ownership and reflection requirements.
We found that intervention depth helps predict task difficulty beyond measured complexity factors, especially between L1 and deeper levels. Cross-system coupling may contribute to this difficulty, but our current evidence cannot confirm its independent effect. The matched-pair success difference is inconclusive (p = 0.49).