acceptodds
Under review as a conference paper at ICLR 2027

FocusTikZ: Quality-Aware Focused Token Optimization for TikZ Code Generation

Abstract

Generating TikZ code from textual descriptions requires models to produce executable code while preserving the intended semantics, spatial organization, and visual appearance of the resulting graphics. Current approaches primarily learn from paired descriptions and reference code, lacking explicit supervision of rendered diagram quality and assigning equal importance to all token positions during optimization. In this paper, we introduce , a quality-aware approach for focused token optimization in TikZ code generation. FocusTikZ assesses generated candidates through compilation and code quality signals, together with three specialized assessment models focused on logic, layout, and style. We further propose Difference-and-Entropy Focused GRPO (DE-GRPO), which identifies informative update positions using reference differences and generation uncertainty. Across multiple benchmarks, FocusTikZ consistently improves both code-level performance and visual fidelity relative to general-purpose and task-specific baselines, with the same trend further supported by human evaluation.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Policy Optimization, Reward Design, Code Generation

Reviews

Among:
Shape:
1234this paper, Top 17%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.75 over 4 reviews, above 83% of the others.
Reviewer_K18aOpenReview ↗
Rating
2
Confidence
4
Informativeness
1(−1)
Presentation
2
Soundness
1(−1)
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Paper summary

This paper presents FocusTikZ, a reinforcement learning framework for text-to-TikZ code generation. The method introduces a quality-aware reward that combines compilation success, code similarity, and three learned assessment models for logic, layout, and style. It further proposes Difference-and-Entropy Focused GRPO (DE-GRPO), which selectively optimizes tokens that differ from the reference code and exhibit high generation uncertainty. Experiments on SKeTikZ and three additional benchmarks demonstrate improvements in code quality, compilation success, and visual fidelity over general-purpose and task-specific baselines.

Critical strengths

1: Practical and well-motivated task. The paper addresses the challenge of generating executable and visually faithful TikZ diagrams, where syntactic correctness alone does not guarantee semantic or structural accuracy.

2: Consistent empirical improvements. FocusTikZ achieves competitive results across multiple benchmarks, outperforming strong task-specific baselines such as TikZilla on several visual quality metrics. The improvements are further supported by human evaluation.

3: Reasonably comprehensive experimental analysis. The paper includes ablations on training stages, reward components, and token selection strategies, as well as additional evaluations of the assessment models and repeated-run results.

Critical weaknesses

1: Limited methodological novelty. The central idea of selectively optimizing informative tokens in GRPO has been explored in prior works, including high-entropy token optimization and critical-token selection for visual generation. DE-GRPO primarily combines reference-based token differences with an existing entropy-based selection strategy. The paper does not sufficiently establish what fundamental methodological insight this combination introduces beyond existing approaches.

2: Insufficient justification for the token selection strategy. Reference differences do not necessarily indicate incorrect or visually important tokens, as different TikZ implementations can produce equivalent diagrams. Similarly, high entropy does not necessarily imply greater impact on visual quality. The intersection of these two sets is therefore largely heuristic. Although the ablations demonstrate its effectiveness, they do not establish that the selected tokens are genuinely more important to diagram quality.

3: Limited visual grounding of the quality reward. Despite emphasizing rendered diagram quality, the three assessment models evaluate textual descriptions and generated code rather than the rendered images themselves. Stronger comparisons with directly image-based reward models would be valuable.

  1. Token Reward Design. The proposed token reward is essentially a code-level similarity measure based on the Jaccard similarity between token sets. However, this approach ignores token order, frequency, and structural relationships. What motivates this design, and what advantages does it offer over n-gram-based metrics or structure-aware alternatives such as AST similarity? A comparative experiment would help justify this choice.

  2. Limited qualitative examples and diagram diversity. More qualitative comparisons would help demonstrate the superiority of the proposed method over existing baselines. Additionally, the evaluated diagram types are relatively limited, and broader coverage would strengthen the evaluation.

Questions for authors

See weakness above.

6 comments
AuthorsOpenReview ↗

Response to Reviewer K18a (W1 and W2)

Dear Reviewer K18a,

Thank you for your valuable feedback. We are pleased that you recognized the practical motivation, consistent empirical improvements, and comprehensive experimental analysis. We address your concerns point by point below.

[Weakness 1] Novelty relative to existing token-selection methods

Beyond the 80/20 Rule selects high-entropy tokens for reasoning updates, while Group Critical-token Policy Optimization for Autoregressive Image Generation (GCPO) selects critical image tokens and adjusts token-level advantages.

TikZ code combines predictable syntax with diagram-specific coordinates, connections, and styles. Short fragments in the latter group can affect multiple rendered elements. Reference alignment filters out code fragments matching the reference, while entropy prioritizes uncertain decisions among the remaining tokens. Our method builds on these characteristics to select key token positions for more efficient policy updates.

Table 8 shows gains over entropy-only selection and controls with equal token budgets. Table 23 supports retaining entropy filtering, while Tables 24–25 show larger rendering changes from resampling selected positions. Together, these results demonstrate the effectiveness of our selection mechanism.

Revision: Based on this discussion, we strengthened the motivation and comparison with prior methods in the Introduction, lines 79–96. Table 8 and Section 5.5 present the supporting ablations, with further sensitivity and resampling results in Tables 23–25. Section 3.3 and Appendix A.3 explain the selection mechanism and its differences from prior methods.

[Weakness 2] Visual relevance of the selected positions

We train controls by sampling the same number of tokens as DE-GRPO from the union of reference-difference and high-entropy positions, all eligible positions, or positions outside its mask, with the same loss normalization and other settings.

Matched-budget controls from revised Table 8.

SelectionLPIPS ↓PSNR ↑MS-SSIM ↑CSR ↑
DE-GRPO0.18926.4990.8280.963
Union0.19825.9310.8070.943
Random0.20525.3760.7970.903
Unselected0.22425.1640.8030.912

DE-GRPO outperforms all controls, showing that the selected positions matter beyond update sparsity or count-dependent normalization.

We additionally mask DE-selected, random, or unselected positions in SFT-generated code under equal masking budgets and resample them with Qwen2.5-Coder-7B, preserving the remaining code.

Comparison with reference code and images from revised Table 24.

Resampled positionsEditDist. ↓PSNR ↑MS-SSIM ↑
Original SFT output68.52825.0350.791
DE-selected69.75023.6280.753
Random72.05224.7520.779
Unselected71.80924.0980.782

Comparison with original SFT code and images from revised Table 25.

Resampled positionsEditDist. ↓PSNR ↑MS-SSIM ↑
DE-selected14.81535.3560.893
Random10.63943.6520.917
Unselected10.55647.4160.945

Under equal masking budgets, resampling DE-selected positions produces larger rendering changes and greater losses in reference-image fidelity. Together with the training controls, this supports their visual relevance. Figures 22–23 illustrate the affected code fragments and renderings.

Revision: Table 8 and Appendix G.5, lines 1881–1893, report matched-budget controls; Tables 24–25 and Appendix G.7, lines 1921–1964, report resampling. Figures 22–23, lines 1992–1995 and 2022–2024, provide qualitative evidence.

AuthorsOpenReview ↗

Response to Reviewer K18a (W3, W4 and W5)

[Weakness 3] Visual validation and comparison with VLM rewards

We collected 250 generated candidates on 50 prompts from five models. Fifteen annotators rated logic, layout, and style from descriptions and rendered diagrams; AMs scored description–code pairs. Both human and AM scores were normalized.

Within-prompt agreement from revised Table 6. PA measures pairwise agreement excluding human-tied pairs; pooled tau-b retains tie correction.

DimensionPA (%) ↑Pooled tau-b ↑
Logic95.120.8952
Layout95.770.9117
Style97.340.9364
Overall quality96.400.9280

AM rankings closely track human visual judgments. Within-model correlations in Table 7 also remain strong across every generator.

We replace only the quality reward with an LLM judge (Qwen2.5-Coder-7B) or VLM judge (Qwen3-VL-8B), keeping other settings unchanged. The VLM receives the description and rendered image, scores each dimension from 0 to 4, and sums the scores after dividing each by 4. The LLM baseline was already included in Figure 4(b) and analyzed in Appendix E.4.

Quality-reward comparison from revised Table 8.

Quality rewardLPIPS ↓PSNR ↑MS-SSIM ↑CSR ↑
LLM-as-a-Judge0.21025.5470.8060.960
VLM-as-a-Judge0.24225.1390.8090.941
Three AMs0.18926.4990.8280.963

We further compare the AM- and VLM-reward generators on 200 shared prompts using DeepSeek-V4.1-Flash as an independent description–image judge.

Description-based error rates from revised Table 5 (%).

RewardNode ↓Edge ↓Relation/layout ↓Label ↓Style ↓Fully compliant ↑
VLM34.031.039.011.58.538.5
AMs29.522.035.07.54.055.5

Error categories may overlap; fully compliant means no identified error. AM rewards yield better generation metrics and fewer description violations than the tested VLM reward, supporting effective visual-quality supervision.

Revision: Tables 5–8; Appendix G.4, lines 1842–1877; Section 5.5, lines 519–528; and Appendix G.2, lines 1784–1809, report these analyses.

[Weakness 4] Jaccard reward motivation and AST comparison

Different TikZ command orders can render the same diagram. Unlike order-sensitive n-gram matching, Jaccard supplies an order-insensitive overlap signal. The initially lower AM rewards in Figure 24 further motivate complementary code-level guidance early in RL.

We replace only Jaccard with normalized AST similarity in [0,1], keeping other settings unchanged.

Auxiliary reward ablation from revised Table 26.

Auxiliary rewardLPIPS ↓PSNR ↑MS-SSIM ↑CSR ↑
Jaccard0.18926.4990.8280.963
Normalized AST0.19526.3570.8170.952
None0.20426.1260.8140.932

Both auxiliary rewards improve over removing the term, while Jaccard performs best in this comparison, supporting its complementary role alongside quality assessment.

Revision: Table 26 and Appendix G.8, lines 2029–2053, explain the design and comparison; Figure 24, lines 2089–2090, shows the reward trajectories.

[Weakness 5] Qualitative coverage and diagram diversity

Figure 25 adds comparisons with DeepSeek-V3, Qwen3-Max, and GPT-5.4-Thinking across graphs, geometry, grid paths, scientific plots, bar charts, and function plots. Appendix E.5 also evaluates external-benchmark diagram types not represented in the SKETIKZ test set.

Cross-type results from revised Tables 16 and 18.

DatasetMethodLPIPS ↓PSNR ↑MS-SSIM ↑
DaTikZ-V1Llama-3.1-Instruct0.18826.0590.849
DaTikZ-V1DiagramCodeAgent0.29422.0160.736
DaTikZ-V1FocusTikZ0.16326.9700.866
DiagramGenLlama-3.1-Instruct0.32021.8320.718
DiagramGenDiagramCodeAgent0.37019.1690.633
DiagramGenFocusTikZ0.30722.2270.725

FocusTikZ leads on LPIPS, PSNR, and MS-SSIM in both cross-type subsets, supporting broader diagram coverage beyond the main benchmark.

Revision: Figure 25 and Appendix G.10, lines 2142–2155, expand qualitative coverage. Appendix E.5, lines 1486–1514, explains the type-based evaluation; Tables 16 and 18, lines 1583–1598 and 1638–1653, report cross-type results.

Thank you for the response. However, it still does not fully address my major concerns.

Weaknesses 4 and 5 have been mostly addressed.

Regarding Weaknesses 2 and 3, I appreciate the additional experiments. However, I still do not see sufficient rationale or diagram-specific adaptation behind the token selection strategy. It still appears to be a relatively straightforward application of an established approach. Moreover, although the authors have added experiments on image-based quality rewards, I believe these should have been included in the original submission, as the paper emphasizes rendered diagram quality while relying on rewards that are not directly related to it. In my view, these two critical weaknesses concern the original motivation and method design, rather than simply a lack of experiments.

My most significant concern remains the novelty and positioning of the paper. After carefully reviewing the paper again, I still find limited methodological novelty in the overall design. This concern cannot be resolved merely by adding further experiments. I also notice that the paper has undergone huge revisions, which raises concerns about the completeness of the initial submission.

Overall, while I appreciate the authors' efforts and additional experiments, I cannot justify a rating higher than 2 based on my assessment. I therefore maintain a negative recommendation.

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

Summary

FocusTikZ targets text-to-TikZ generation: mapping a natural-language description to compilable TikZ code that renders the intended diagram. The paper's two motivating observations are that (i) existing text-to-TikZ systems are trained to imitate a single reference program, although one diagram admits many valid implementations, so lexical similarity is neither necessary nor sufficient for a correct rendering; and (ii) standard GRPO spends its update budget uniformly over all tokens, while in TikZ a large fraction of tokens is constant syntactic scaffolding and only a small subset governs node relations, coordinates, and style. The proposed system is a two-part fix on top of Qwen2.5-Coder-7B: a quality-aware reward, and a token-selective variant of GRPO.

The reward is R_overall = R_success · (R_token + R_quality). Compilation success is a binary gate. R_token is the Jaccard similarity between the generated and reference token sets, deliberately order-insensitive. R_quality is the sum of three learned "assessment models" — logic, layout, style — each a Qwen2.5-Coder-7B encoder plus an MLP that reads description ‖ code ‖ <eos> and scores the <eos> hidden state; the three scores are sigmoid-normalized and summed, so quality carries three times the weight of the token term. The assessment models are trained with a Bradley-Terry pairwise ranking loss against synthetic negatives produced by an LLM multi-agent pipeline (Describe → Plan → Edit, with a compilation gate and manual graduate-student screening to confirm each perturbation touches only its target dimension): 2,111 logic, 2,264 layout, 2,376 style negatives over 2,585 training references.

DE-GRPO then restricts updates to focused token sets. For each candidate, T_diff is the set of generated tokens that differ from the reference after LCS-anchored alignment; T_ent is the top-20% highest-entropy positions under the current policy; the update applies the usual clipped GRPO surrogate and trajectory-level advantage, but normalized over T_i = T_diff ∩ T_ent rather than over the whole sequence, with a fallback to the union when the intersection is empty. The paper is careful to state that difference tokens are localization priors, not errors, so a valid alternative implementation can still receive positive advantage.

Contributions

  1. Reframes text-to-TikZ supervision away from reference imitation toward rendered-diagram quality, with compilation gated in.
  2. Three decoupled, contrastively trained quality assessment models built on a purpose-made multi-agent negative-construction pipeline with per-dimension perturbation control and cross-family validation sets.
  3. DE-GRPO: token-level credit assignment combining reference-difference localization with entropy-based uncertainty, applied as a modification of the GRPO objective.
  4. An evaluation spanning SKETIKZ plus three cross-distribution datasets, 15+ baselines including task-specific systems, image-level and code-level metrics, a human study, and cost reporting.

Validation

Setup: SKETIKZ (2,585 train / 323 test) as the main benchmark, with cross-dataset tests on DATIKZ-V1, DATIKZ-V4 and DiagramGenBenchmark; nine metrics across code similarity (ROUGE-L, EditDist, chrF, CrystalBLEU), executability (CSR), and rendered-image similarity (CLIPScore, LPIPS, PSNR, MS-SSIM); baselines spanning zero-shot coder/chat/commercial LLMs (up to GPT-5.4, DeepSeek-V3, Qwen2.5-Instruct-72B) and TikZ-specific systems (CLiMA-7B/13B, DiagramCodeAgent, TikZilla-8B). Training is PEFT: SFT 10 epochs, RL 3 epochs with 16 samples per prompt; cost reported as 12h/1 GPU for assessment models, 6h for SFT, 48h on 8×A100 for RL.

Results: on SKETIKZ FocusTikZ-7B leads every column — ROUGE-L 45.553, CSR 0.963, CLIPScore 0.872, LPIPS 0.189, MS-SSIM 0.828 — ahead of TikZilla-8B by 1.7 ROUGE-L, 0.053 CSR and 0.077 LPIPS, and ahead of its own base model by 6.1 ROUGE-L and 0.156 CSR. It also leads on all three cross-distribution sets, including the out-of-type subsets, and wins the human study (3.496 vs 3.283 for GPT-5.4, 3.162 for TikZilla, 2.919 for standard GRPO, over 15 annotators × 50 samples per model).

Ablations: removing SFT costs 6.10 ROUGE-L, removing RL 7.22; removing R_success 3.07 but R_token only 0.86; and on token selection, standard GRPO 43.684, entropy-only 44.595, difference-only 44.698, union 44.362, full intersection 45.553 (CrystalBLEU separates the same ordering more sharply, 25.484 → 29.986). Five-seed variances are given for FocusTikZ and standard GRPO (±0.638 ROUGE-L), so the +1.87 DE-GRPO gain is roughly 3σ. Appendix adds assessment-model accuracy on two held-out perturbation sets, reward-human correlation (Pearson 0.950), an LLM-as-judge replacement that underperforms with an explanation in terms of score-distribution narrowness, per-diagram-type breakdowns, and a worked example of which tokens get selected.

the engineering is solid and the evaluation is broader than typical for this task, but the evidence is measured almost entirely against reference code and reference renderings — the same object the paper argues is the wrong target. Every one of the nine automatic metrics compares to the reference, the human study asks annotators for similarity to the ground-truth diagram, and nothing measures whether the rendered diagram satisfies the input description. Add that image-level metrics are computed after excluding non-compiling samples, which puts models with CSR 0.21–0.37 on a different and easier denominator than FocusTikZ's 0.963, that the assessment models saturate at 100% on one of their two validation sets, that no reward-hacking analysis accompanies RL against a frozen learned reward, and that the entropy-only variant already captures about half the DE-GRPO gain (and reproduces a published finding), and the contribution looks narrower and less secure than the framing. The strongest parts are the negative-construction pipeline with cross-family validation and the clean four-way token-selection ablation.

Critical strengths

First, the token-selection ablation is a clean, well-isolated experiment that yields a finding of use beyond this paper. With reward, data, base model, and budget held fixed, standard GRPO scores 43.684, entropy-only 44.595, difference-only 44.698, union 44.362, intersection 45.553, and CrystalBLEU separates the same ordering more sharply (25.484 → 29.986). Two things follow that I did not know before reading: the two signals are complementary rather than redundant, since either alone leaves roughly half the gain on the table; and taking their union is worse than taking either alone, which is the opposite of the intuitive damping strategy and is exactly what a practitioner would have implemented by default. Why this is consequential: it is a comparison among variants trained and evaluated identically, so its internal ordering is valid even if the absolute metrics are contested — the reference-circularity objection that anchors my skepticism does not dissolve the fact that one token-selection rule beats another under matched conditions. It also independently corroborates the paper's premise that TikZ tokens are highly unequal in decision value, which is the assumption the whole framing rests on. A paper that establishes one robust, transferable micro-result about credit assignment granularity has contributed something even if its headline claim shakes out to be partly an artifact of its metric choice.

Second, the negative-construction pipeline plus the judge post-mortem is where this paper produces knowledge that outlives the model it trains. The Describe → Plan → Edit decomposition with a compilation gate and human screening produces single-dimension perturbations (2,111 / 2,264 / 2,376 for logic / layout / style) whose quality is then checked by building validation sets with a different model family, so that any assessment model that succeeds on them demonstrably generalizes across pipelines rather than learning one generator's fingerprint. Alongside it, Appendix E.4's analysis of why LLM-as-judge fails as a reward here is a concrete result I can carry to other work: the judge's normalized scores have mean 0.804 and variance 0.010, so within a group of 16 candidates the advantage is nearly pure noise, whereas a pairwise-trained model spreads scores enough to rank. Why this is consequential: my rejection case is essentially that the reward is validated only against artifacts it was built from, and this is the one part of the paper that argues against that reading with evidence rather than assertion. It is also the reusable artifact — the negative data and the reward-model training procedure — that other groups in text-to-diagram, and more broadly in learned-reward RL for structured generation, would actually adopt.

Critical weaknesses

Weakness 1 — the evaluation measures the training target, not the claimed target.

Section 3.2 argues at length that reference resemblance is neither necessary nor sufficient for a good diagram, and that this is precisely why reinforcement learning is needed here. Every piece of evidence subsequently offered contradicts that premise. The nine automatic metrics are reference distances: ROUGE-L, EditDist, chrF, and CrystalBLEU compare generated code to reference code, and CLIPScore, LPIPS, PSNR, and MS-SSIM compare the rendered output to the rendering of the reference code. The human study asks 15 annotators to rate "overall similarity and visual fidelity to the ground-truth reference diagram." Nothing anywhere measures whether the rendered diagram satisfies the input description — no VLM judge over (description, image), no constraint-level check on the rendered output, no semantic error taxonomy. Meanwhile the reward being optimized contains a Jaccard-to-reference term and three assessment models trained with a Bradley-Terry objective that rewards the reference code over perturbed variants. So training pushes toward reference proximity and evaluation scores reference proximity; the measured construct and the optimized construct are the same construct. Consequential because it is not a gap in coverage, it is a possible explanation for the entire result: FocusTikZ may simply have learned to produce outputs that look more like reference diagrams, which is a different achievement from producing diagrams that better realize the description, and the paper's own motivation says the difference matters. It also means the framing has to change — the honest headline is "closer to reference renderings at higher compilation rate," which is a legitimate result but a much smaller one, and it is the opposite of what the introduction promises.

Weakness 2 — the quality reward is validated only against artifacts it was built from, and its behavior during optimization is never monitored.

The three assessment models are the mechanism that is supposed to supply diagram-quality supervision beyond the reference, so their validity is the load-bearing assumption. The evidence offered is a validation set on which all three views score 100.00%, and a second on which they score 91–94–100% (Table 8). A saturated benchmark says nothing about discriminative power, and perfect accuracy on three independent dimensions is more consistent with the negatives being separable by shallow surface pattern than with the models capturing logic, layout, and style. The human-alignment table is the intended rebuttal, but it reports means for five models and a "sample-level" Pearson of 0.950 without stating whether clustering by model is controlled, so between-model spread alone could produce that number. Against this thin validation sits an RL run of three epochs with 16 samples per prompt against a frozen learned reward — the textbook setup for reward hacking — and the paper reports no reward-versus-iteration curve, no comparison of assessment-model scores to human ratings across training checkpoints, and no drift analysis. Compounding it, the empty-intersection fallback to the union is disclosed only in Appendix E.2 and never quantified, so the frequency with which DE-GRPO is not the algorithm described in Section 3.3 is unknown. Consequential because these two weaknesses multiply: if the reward is a proxy that the policy can exploit, and the evaluation shares the reward's reference bias, then the reported gains cannot distinguish "the reward is a good proxy and RL exploited it well" from "the reward is a bad proxy and RL exploited it" — and that distinction is the paper's scientific content.

Questions for authors
  1. Can you evaluate the rendered diagrams against the input description rather than against the reference? You already have all generated outputs, so this needs no retraining: a VLM or LLM judge scoring (description, rendered image) for semantic compliance, ideally with a small human check, plus a per-sample error taxonomy (wrong node, reversed edge, missing relation, wrong label). If FocusTikZ leads there as well, my central objection largely dissolves and the paper becomes considerably stronger. If the gains over TikZilla and GPT-5.4 are concentrated in reference similarity and do not survive a description-based check, then the headline has to be re-aimed, and I would rather know that from you than infer it. Please also say what fraction of outputs are semantically correct in absolute terms, not only relative to the reference.

  2. Can you show the comparison restricted to the cases where reference metrics are least meaningful? Specifically, stratify per-sample results by code edit distance to the reference (or by whether the generated program uses structurally different constructs, e.g. \foreach versus explicit \node sequences) and report whether FocusTikZ's advantage over TikZilla persists in the high-dissimilarity stratum. A model that wins only where its output resembles the reference is consistent with my reading; a model that wins in the stratum where the reference is a poor guide would be strong evidence against it.

  3. Please report the image-level metrics under a denominator that does not depend on compilation success — every sample scored, with failures assigned the worst value, or at minimum both variants side by side. Your E.2 note excludes non-compiling samples, and CSR ranges from 0.205 to 0.963 across your baselines, so the current comparison is undefined across models even if, as I suspect, the bias favors your competitors. This is cheap and removes an ambiguity I otherwise have to hold against the paper.

  4. What happens to your assessment models on negatives they were not built to detect? Table 8's 100.00% on all three GenCode views tells me the perturbations are separable, not that the models measure quality. The test that matters is pairwise accuracy where the "negative" is a different but valid implementation, or a genuinely wrong diagram authored or labeled by humans rather than generated by your Edit Agent. Relatedly, please give the reward-human correlation computed within models (or with model identity as a random effect): Table 10(a) aggregates five model-level means, and between-model spread alone could produce Pearson 0.950.

Suggestions for future work — explicitly not required for my assessment, and I will not penalize their absence: re-instantiating the framework for SVG, Mermaid, or Graphviz; extending to multimodal or agentic diagram editing; a theoretical account of why difference-and-entropy intersection beats either signal alone; scaling to larger base models; and releasing the negative dataset and assessment-model weights so that others can test the reward independently of the policy. The last is the item I would most like to see eventually, because your reward models are the reusable contribution, but it is not something I would hold against this submission.

2 comments
AuthorsOpenReview ↗

Response to Reviewer rjUZ(W1 & Q1 and Q2)

Dear Reviewer rjUZ,

Thank you for your valuable feedback. We are pleased that you recognized the complementary token-selection signals and the value of our negative-construction pipeline and reward-model analysis. We address your questions point by point below.

[Weakness 1 & Question 1] Compliance with input descriptions

We evaluate five generators on the same 200 SKETIKZ prompts. T2I measures description–image similarity using frozen CLIP encoders. DeepSeek-V4.1-Flash scores description compliance from 1 to 5 and identifies errors, receiving the input description and rendered image.

Description alignment from revised Table 4.

MethodT2I ↑VLM score ↑
Qwen2.5-Coder-7B0.6822.365
Standard GRPO0.8063.065
GPT-5.40.8203.275
TikZilla0.8093.160
FocusTikZ0.8463.490

We manually audited 100 randomly selected results from the 1,000 VLM alignment scores with generator identities hidden. The audited scores were broadly consistent with human judgments, with no extreme discrepancies observed.

Description-based errors and full compliance from revised Table 5 (%).

MethodNode ↓Edge ↓Relation/layout ↓Label ↓Style ↓Fully compliant ↑
Qwen2.5-Coder-7B56.548.571.025.514.013.5
Standard GRPO45.537.057.516.512.018.0
GPT-5.440.029.044.59.05.048.0
TikZilla42.038.551.513.512.540.5
FocusTikZ29.522.035.07.54.055.5

Error rates count outputs with at least one error in each category; categories may overlap. Fully compliant denotes outputs judged to have none of these errors. FocusTikZ leads on description alignment, every error category, and full compliance, supporting improvements in satisfying the input description.

Revision: Tables 4–5 and Appendix G.2, lines 1784–1809, report the evaluation and human audit.

[Question 2] Performance at high reference-code dissimilarity

We stratify 200 jointly compilable prompts by FocusTikZ's normalized reference-code edit distance: Low (d≤55d\leq55, 50 prompts), Medium (55<d<7055<d<70, 100), and High (d≥70d\geq70, 50).、

High-dissimilarity results from revised Table 22.

MethodLPIPS ↓PSNR ↑MS-SSIM ↑T2I ↑
TikZilla0.37522.2060.7760.763
GPT-5.40.43518.2960.6060.804
FocusTikZ0.28422.9020.7950.824

FocusTikZ leads across all three strata, including in description–image alignment at high edit distance. Its advantage is therefore not confined to outputs whose code closely resembles the reference.

Revision: Table 22 and Appendix G.3, lines 1813–1838, report all strata and the grouping protocol.

AuthorsOpenReview ↗

Response to Reviewer rjUZ (Q3 and W2 & Q4)

[Question 3] Evaluation with a compilation-independent denominator

We report Individual evaluation on each method's successfully compiled outputs alongside Full evaluation over all test prompts. Under Full, failed renderings are replaced with blank images.

Image-level results from revised Table 21 (Individual / Full).

MethodCLIPScore ↑LPIPS ↓PSNR ↑MS-SSIM ↑
Standard GRPO0.847 / 0.8410.212 / 0.22425.173 / 24.9150.792 / 0.784
TikZilla0.862 / 0.8570.266 / 0.28625.309 / 24.7300.817 / 0.807
GPT-5.40.837 / 0.8290.375 / 0.40620.815 / 20.0710.641 / 0.628
FocusTikZ0.872 / 0.8650.189 / 0.19326.499 / 26.5260.828 / 0.823

FocusTikZ remains best on every image metric when every test prompt is included.

Revision: Table 21 and Appendix G.1, lines 1749–1781, present all three protocols and their results.

[Weakness 2 & Question 4] AM validation beyond constructed negatives

We collected 250 naturally generated candidates on 50 test prompts from five models. The pool includes human-verified distinct valid implementations, rather than Edit Agent perturbations. Fifteen annotators rated logic, layout, and style from descriptions and rendered diagrams; AMs scored description–code pairs. Both human and AM scores were normalized.

Within-prompt ranking from revised Table 6. PA is agreement on human-non-tied pairs; pooled Kendall's tau-b aggregates within-prompt pair counts with tie correction.

DimensionNon-tied pairsPA (%) ↑Pooled tau-b ↑
Logic49295.120.8952
Layout49695.770.9117
Style48997.340.9364
Overall quality50096.400.9280

AM rankings closely track human visual judgments on naturally generated alternatives, beyond the constructed-negative validation.

We also correlate overall AM and human quality scores separately within each generator, using its 50 candidates.

Within-model correlations from revised Table 7.

Generating modelPearson's r ↑Spearman's rho ↑
FocusTikZ0.8960.941
Qwen2.5-Coder-7B0.8870.948
DeepSeek-V30.9050.933
Qwen3-Max0.8970.924
GPT-5.40.8930.932

AM scores correlate strongly with human judgments within every generator, so agreement is not solely driven by between-model quality differences.

Revision: Tables 6–7 and Appendix G.4, lines 1842–1877, report both analyses.

[Weakness 2] Reward monitoring and fallback frequency

We added the three AM reward trajectories and evaluated successive RL checkpoints using the same evaluation protocol.

Selected checkpoint results from revised Table 27.

RL epochsLPIPS ↓PSNR ↑MS-SSIM ↑CSR ↑
10.20926.0170.7920.875
20.19126.2260.8250.958
3 (FocusTikZ)0.18926.4990.8280.963

Reward trajectories fluctuate, but all reported generation metrics improve across checkpoints. This supports continued gains in executability and reference fidelity.

The union fallback was never triggered in the reported training runs; every update mask used the intersection.

Revision: Figure 24, Table 27, and Appendix G.9, lines 2057–2095, report training monitoring; Appendix E.2, lines 1333–1336, defines the fallback.

Reviewer_aPUAOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
1
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces FocusTikZ, a reinforcement learning framework for generating executable TikZ code from natural-language descriptions. The proposed approach combines two main components: (1) a quality-aware reward function incorporating compilation success, token-level similarity, and three learned assessment models evaluating diagram logic, layout, and style; and (2) Difference-and-Entropy Focused GRPO (DE-GRPO), which selectively optimizes tokens that differ from the reference code and exhibit high generation entropy. The assessment models are trained using synthetically generated negative examples, while the generation model is initialized through supervised fine-tuning before RL optimization.

The authors evaluate FocusTikZ on four benchmarks: SKeTikZ, DaTikZ-V1, DaTikZ-V4, and the DiagramGen Benchmark. The reported results show improvements over general-purpose and task-specific baselines across code-level metrics, compilation success, and rendered-diagram fidelity. These findings are further supported by human evaluations and ablation studies examining the contributions of individual reward components, training stages, and token-selection strategies.

Critical strengths

strong empirical results: The paper demonstrates strong empirical results across several benchmarks, consistently outperforming both general-purpose LLMs and specialized TikZ generation models. These improvements extend beyond code-level similarity to compilation success and rendered-diagram quality, with additional support from human evaluations. The extensive ablation studies further suggest that different components of the proposed framework contribute to the overall performance.

Critical weaknesses

insufficient analysis: Although the authors provide relatively extensive ablation studies demonstrating the empirical benefits of their components, these experiments primarily measure downstream task performance without sufficiently validating the proposed token-selection mechanism. In particular, high token entropy does not necessarily imply causal importance for the final generation quality, and differences from a reference implementation do not necessarily indicate incorrect or consequential decisions. Moreover, DE-GRPO applies the same trajectory-level advantage to all selected tokens rather than explicitly estimating their individual contributions to the outcome. While the appendix includes qualitative examples of selected tokens, more targeted experiments are needed to establish that the proposed selection criterion identifies genuinely important positions. For example, comparing against random token selection under a matched token budget and measuring the effect of perturbing selected versus excluded tokens on final diagram quality would provide stronger evidence for the proposed mechanism.

insufficient positioning relative to existing literature: The proposed framework primarily combines two established ideas: learned reward modeling, commonly used in RLHF, and non-uniform token optimization, previously explored in the RL literature. In particular, entropy-guided token selection has already been studied in prior work [1,2]. Although the authors acknowledge some of these connections in the appendix, the main methodology section does not adequately contextualize the proposed techniques or clearly distinguish their contributions from existing approaches.


[1] Tan, Hongze, and Jianfei Pan. "Gtpo and grpo-s: Token and sequence-level reward shaping with policy entropy." ICML 2025.

[2] Liu, Zheng, et al. "Heterogeneous Adaptive Policy Optimization: Tailoring Optimization to Every Token’s Nature." ACL 2026.

Questions for authors

validity of the token-selection criterion: The motivation behind DE-GRPO is that selected tokens are more consequential for the final diagram quality. However, high entropy does not necessarily imply causal importance, and differences from a reference implementation do not necessarily indicate important decisions. Beyond the qualitative examples in Appendix E.6, can the authors provide evidence that selected tokens have a greater influence on the final outcome than excluded tokens? For instance, measuring changes in diagram quality when perturbing or resampling selected versus excluded tokens would help validate this hypothesis.

controlled token-selection ablations: While Table 4 provides extensive ablations, it remains unclear whether DE-GRPO's improvements arise from identifying genuinely informative tokens or simply from optimizing fewer token positions. Could the authors compare against random token selection with a matched token budget? Additionally, how sensitive are the results to the choice of the top 20% entropy threshold, which appears to be adopted from prior work on LLM reasoning?

novelty relative to existing RL methods: The proposed framework combines learned reward modeling, widely studied in the RLHF literature, with selective token optimization. In particular, entropy-guided token selection has already been explored in prior work [1,2]. Could the authors clarify the methodological novelty of DE-GRPO beyond combining high-entropy token filtering with reference-based difference detection? How does this combination advance the existing literature on token-level optimization?


[1] Tan, Hongze, and Jianfei Pan. "Gtpo and grpo-s: Token and sequence-level reward shaping with policy entropy." ICML 2025.

[2] Liu, Zheng, et al. "Heterogeneous Adaptive Policy Optimization: Tailoring Optimization to Every Token’s Nature." ACL 2026.

4 comments
AuthorsOpenReview ↗

Response to Reviewer aPUA (W1 & Q1 and W1 & Q2)

Dear Reviewer aPUA,

Thank you for your valuable feedback. We are pleased that you recognized our strong results across benchmarks and the support from human evaluation and ablations. We address your questions point by point below.

[Weakness 1 & Question 1] Visual impact of the selected tokens

We mask DE-selected, random, or unselected token positions in code generated by the SFT model and resample the masked spans using Qwen2.5-Coder-7B to compare the rendered images before and after resampling.

Comparison with the reference code and image from revised Table 24.

Resampled positionsEditDist. ↓PSNR ↑MS-SSIM ↑
Original SFT output68.52825.0350.791
DE-selected69.75023.6280.753
Random72.05224.7520.779
Unselected71.80924.0980.782

Comparison with the original SFT code and image from revised Table 25.

Resampled positionsEditDist. ↓PSNR ↑MS-SSIM ↑
DE-selected14.81535.3560.893
Random10.63943.6520.917
Unselected10.55647.4160.945

Resampling DE-selected positions produces larger rendering changes and greater losses in reference-image fidelity under the same masking budget, supporting their visual relevance.

Revision: Tables 24–25 and Appendix G.7, lines 1921–1964, report the experiment; Figures 22–23, lines 1992–1995 and 2022–2024, illustrate the affected code and renderings.

[Weakness 1 & Question 2] Matched-budget controls and entropy-ratio sensitivity

We train controls by uniformly sampling the same number of tokens as DE-GRPO from the union of reference-difference and high-entropy positions, all eligible positions, or positions outside the DE-GRPO mask.

Selected results from revised Table 8.

SelectionLPIPS ↓PSNR ↑MS-SSIM ↑CSR ↑
DE-GRPO0.18926.4990.8280.963
Union0.19825.9310.8070.943
Random0.20525.3760.7970.903
Unselected0.22425.1640.8030.912

DE-GRPO outperforms all three controls across every reported metric, supporting the value of the selected positions beyond update sparsity or count-dependent normalization.

We also vary the high-entropy candidate ratio while keeping other settings unchanged. This ratio determines the candidate set before intersection with reference-difference positions, rather than the final update count.

Selected results from revised Table 23.

Entropy ratioLPIPS ↓PSNR ↑MS-SSIM ↑CSR ↑
10%0.19826.1070.8160.929
20%0.18926.4990.8280.963
50%0.20126.0470.8200.955
100% (difference-only)0.20226.2760.8130.948

The default 20% performs best among the tested ratios. Both narrower selection and weaker entropy filtering reduce performance, providing TikZ-specific support for this choice.

Revision: Tables 8 and 23 and Appendices G.5–G.6, lines 1881–1917, report these controls and the sensitivity analysis.

AuthorsOpenReview ↗

Response to Reviewer aPUA (W2 & Q3)

[Weakness 2 & Question 3] Novelty relative to existing token-level optimization

GTPO and GRPO-S uses entropy to reshape token-level or sequence-level rewards. HAPO adapts sampling, advantage estimation and redistribution, and clipping using token-level signals.

TikZ code combines predictable syntax with diagram-specific coordinates, connections, and styles. Short fragments in the latter group can affect multiple rendered elements. Reference alignment filters out code fragments matching the reference, while entropy prioritizes uncertain decisions among the remaining tokens. Our method builds on these characteristics to select key token positions for more efficient policy updates.

Table 8 shows that DE-GRPO outperforms controls with equal token budgets. The single criterion and entropy ratio ablations in Tables 8 and 23 favor combining reference differences with uncertainty. Tables 24–25 show that resampling selected positions causes larger rendering changes. Together, these results demonstrate the effectiveness of our method.

Revision: Based on this discussion, we strengthened the motivation and comparison with prior methods in the Introduction, lines 79–96. Table 8 and Section 5.5 present the supporting ablations, with further sensitivity and resampling results in Tables 23–25. Section 3.3 and Appendix A.3 explain the selection mechanism and its differences from prior methods.

Thank you for the detailed response. The rebuttal has convincingly addressed my concern that DE-GRPO's improvements might simply result from optimizing fewer token positions. I appreciate the additional experiments and will therefore raise my score to 3.

That said, I still believe the contribution is better characterized as a useful and empirically validated adaptation of existing selective RL optimization techniques to diagram generation, rather than a fundamentally new approach to token-level policy optimization.

I personally value applied research, and I believe this work has merit from that perspective. I would encourage the authors to provide a more comprehensive discussion of related work and position their contribution more clearly within the existing literature.

Thank you for your reply and valuable suggestions. We will further polish the manuscript and strengthen the discussion of related work.

Reviewer_Hr4vOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

FocusTikZ trains a text-to-TikZ model with supervised fine-tuning followed by reinforcement learning. Its reward combines compilation success, reference-token overlap, and learned assessments of logic, layout, and style. Difference-and-Entropy Focused GRPO selects update positions using reference-code differences and token entropy, falling back to their union when the intersection is empty. Evaluation on SKETIKZ and external benchmarks covers code similarity, rendered-image quality, compilation, and human judgments. Ablations examine the training stages, rewards, and token-selection rules.

Critical strengths
  1. The reward design addresses several distinct failure modes. Compilation gating handles invalid outputs, while separately trained assessment models target logic, layout, and style. Their negative examples are constructed by aspect and manually inspected, providing supervision for diagram defects that would be difficult to capture through token overlap alone.
  2. On SKETIKZ, FocusTikZ improves over standard GRPO in compilation success, from 0.921 to 0.963; LPIPS, from 0.212 to 0.189; and PSNR, from 25.173 to 26.499. Table 4 compares difference-only, entropy-only, and union-based selection, making the benefit of the complete recipe reasonably assessable.
  3. The automatic results are accompanied by a blind evaluation with 15 annotators, giving FocusTikZ a mean score of 3.496 versus 2.919 for standard GRPO. External benchmark evaluations and repeated-run results provide additional evidence that the improvements are perceptible and are not confined to a single metric or dataset.
Critical weaknesses
  1. Appendix E.2 excludes noncompiling samples before averaging fidelity metrics. Because compilation rates differ, these averages describe different subsets of prompts. Reporting compilation success separately is helpful, but does not resolve the comparability of the remaining scores. The filtering could affect the ranking in either direction. Results on a common successful-compilation subset, together with an aggregate accounting for every prompt, would make the practical improvement easier to judge.
  2. The ablations do not fully isolate why the token mask helps. High-entropy policy updates have a precedent in Wang et al. (2025), as the paper acknowledges. The difference-only and union comparisons are useful, but the intersection changes both the selected positions and their number, with normalization over that selected set. A mask matched in cardinality would help distinguish the proposed identification of quality-critical tokens from effects of update sparsity and weighting.
  3. The assessment-model validation leaves within-prompt ranking uncertain. Appendix E tests whether reference code scores above erroneous variants, and Table 10 reports encouraging correlations with human ratings. These checks support the reward models, but do not clearly show how reliably they rank two plausible generated solutions to the same prompt. Since the assessors read descriptions and code rather than rendered images, this is relevant to whether they guide subtle visual improvements during RL.
Questions for authors
  1. Do the fidelity rankings persist on a shared successful-compilation subset and under an aggregate that accounts for every prompt?
  2. Does DE-GRPO outperform a random-token mask matched to its selected-token count and normalization?
  3. Does the human-alignment analysis measure within-prompt ranking accuracy between generated candidates, including distinct valid implementations?
2 comments
AuthorsOpenReview ↗

Response to Reviewer Hr4v (W1 & Q1 and W2 & Q2)

Dear Reviewer Hr4v,

Thank you for your valuable feedback. We are pleased that you recognized our complementary reward design and the improvements supported by human evaluation and external benchmarks. We address your questions point by point below.

[Weakness 1 & Question 1] Comparability across compilation-success subsets

We evaluate FocusTikZ, Standard GRPO, TikZilla, and GPT-5.4 under three protocols:

  • Individual: Each method's own successfully compiled outputs, following the original evaluation.
  • Common: The same 278 prompts for which all four methods compile successfully.
  • Full: All 323 test prompts. Code metrics use the original generated code, including failed programs; image metrics replace missing renderings with blank images.

Image-level results from revised Table 21.

ProtocolMethodCLIPScore ↑LPIPS ↓PSNR ↑MS-SSIM ↑
IndividualStandard GRPO0.8470.21225.1730.792
IndividualTikZilla0.8620.26625.3090.817
IndividualGPT-5.40.8370.37520.8150.641
IndividualFocusTikZ0.8720.18926.4990.828
CommonStandard GRPO0.8530.20826.0500.824
CommonTikZilla0.8790.21026.1250.837
CommonGPT-5.40.8430.35421.2810.728
CommonFocusTikZ0.8950.17828.7640.871
FullStandard GRPO0.8410.22424.9150.784
FullTikZilla0.8570.28624.7300.807
FullGPT-5.40.8290.40620.0710.628
FullFocusTikZ0.8650.19326.5260.823

FocusTikZ achieves the best performance across all reported metrics under both Common and Full evaluation protocols.

Revision: Table 21 and Appendix G.1, lines 1749–1781, report the protocols, complete results, and analysis.

[Weakness 2 & Question 2] Token selection under matched counts and normalization

We train control variants with the same settings and token budgets as DE-GRPO, uniformly sampling from the union of reference-difference and high-entropy positions, all eligible output positions, or positions outside the DE-GRPO mask.

Selected results from revised Table 8; all controls match the token count.

SelectionLPIPS ↓PSNR ↑MS-SSIM ↑CSR ↑
DE-GRPO0.18926.4990.8280.963
Union0.19825.9310.8070.943
Random0.20525.3760.7970.903
Unselected0.22425.1640.8030.912

DE-GRPO outperforms all three controls across every reported metric. These results support the value of the selected positions beyond update sparsity or count-dependent normalization.

Revision: Table 8, Section 5.5, lines 480–485, and Appendix G.5, lines 1881–1893, present these controls and their interpretation.

AuthorsOpenReview ↗

Response to Reviewer Hr4v (W3 & Q3)

[Weakness 3 & Question 3] Ranking generated candidates within the same prompt

We added an evaluation of naturally generated candidates, including human-verified alternative implementations satisfying the same description.

Setting. We randomly sampled 50 SKETIKZ test prompts and collected outputs from models including FocusTikZ, Qwen3-Max, and GPT-5.4. Fifteen annotators evaluated the rendered diagrams against their input descriptions, scoring logic, layout, and style. Both human ratings and AM scores were normalized.

We compare only candidates for the same prompt, yielding 500 pairs. Pairwise agreement (PA) is the proportion of human-non-tied pairs on which the AM and human preferences agree. Pooled Kendall's tau-b uses concordant, discordant, and tied-pair counts aggregated across prompt.

Ranking results from revised Table 6.

DimensionHuman-non-tied pairsPA (%) ↑Pooled tau-b ↑
Logic49295.120.8952
Layout49695.770.9117
Style48997.340.9364
Overall quality50096.400.9280

This evaluation relates their preferences to human visual judgments among alternative solutions to an identical description. It extends validation beyond the constructed negative examples used to train the AMs.

Using the same annotations, we also correlate AM quality scores with composite human ratings separately for each generator's 50 candidates. Pearson's r measures linear association; Spearman's rho measures rank association.

Within-model results from revised Table 7.

Generating modelPearson's r ↑Spearman's rho ↑
FocusTikZ0.8960.941
Qwen2.5-Coder-7B0.8870.948
DeepSeek-V30.9050.933
Qwen3-Max0.8970.924
GPT-5.40.8930.932

These results show strong rank correlations between AM scores and human ratings within each model.Together, these analyses support the AMs' ability to rank actual generated solutions consistently with human assessments.

Revision: Tables 6–7 and Appendix G.4, lines 1842–1877, document the candidate collection, scoring, metric definitions, and results.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Brief summary of our rebuttal

Dear Area Chair and Reviewers,

We sincerely thank the reviewers for your time and constructive feedback. We appreciate Reviewers Hr4v and rjUZ for highlighting the strengths of our reward design and token selection strategy, and Reviewers aPUA and K18a for recognizing the gains in diagram quality across benchmarks and the supporting evidence from human evaluations and ablation studies. To assist in facilitating the review process, we’d like to provide a brief summary of the rebuttal:

  1. Do the selected tokens matter for diagram quality? Reviewers Hr4v, aPUA, and K18a raised the concern that DE-GRPO’s gains might stem solely from updating fewer tokens. Reviewers aPUA and K18a also expressed concern that the distinction between DE-GRPO and prior methods was unclear. We clarified how DE-GRPO uses differences from the reference code to identify candidate positions and token entropy to prioritize uncertain decisions. Table 8 of the revised manuscript shows that DE-GRPO outperformed all three selection controls when the token count and loss normalization were held fixed. The resampling experiments in Tables 24 and 25 further show that resampling the selected tokens changed the rendered diagrams more than resampling random or unselected tokens, supporting the visual relevance of the selected positions.

  2. Do the gains hold when evaluation accounts for compilation failures and tests the input description directly? Reviewers Hr4v and rjUZ raised the concern that differences in compilation rates could affect the fidelity comparison. Table 21 shows that FocusTikZ led on all four image metrics on both the full test set and the subset where all methods compiled successfully. We used a vision-language model to assess how well the diagrams matched their descriptions and manually checked the ratings. Tables 4 and 5 report this evaluation. The evaluator judged 55.5% of FocusTikZ outputs fully compliant, compared with 48.0% for GPT-5.4 and 40.5% for TikZilla. Table 22 further shows that FocusTikZ retained its lead even when its generated code differed substantially from the reference.

  3. Do the learned rewards reflect human judgments of rendered diagrams? Reviewers Hr4v, rjUZ, and K18a raised concerns about whether assessors that read TikZ code can reliably judge the visual quality of rendered diagrams. We compared the assessors’ rankings with human judgments of diagrams generated for the same prompt, including distinct valid implementations. Table 6 of the revised manuscript shows that the assessors agreed with human preferences on 96.4% of diagram pairs for overall quality. Table 7 shows that assessor scores also correlated strongly with human ratings within each generator. Finally, the reward comparison in Table 5 shows that training with these assessors yielded fewer violations of the input descriptions across all five error categories than training with the tested image-based reward.

  4. What supports the choice of token reward and the coverage of diagram types? Reviewer K18a raised concerns about the choice of Jaccard similarity and the limited range of diagrams in our visual comparisons. We chose Jaccard similarity as an auxiliary reward because it measures token overlap regardless of command order, and different TikZ command orders can produce the same diagram. Table 26 of the revised manuscript shows that Jaccard similarity outperformed both alternatives we tested, using syntax-tree similarity and omitting the auxiliary reward. We also added visual comparisons across diagram types in Figure 25.

We especially thank Reviewers aPUA and K18a for their prompt replies. Reviewer aPUA confirmed that the controlled experiments addressed the concern about gains from updating fewer tokens. We will follow their suggestion to strengthen the related work discussion. Reviewer K18a noted that the token reward and diagram coverage concerns were largely addressed.

Reviewer K18a also suggested comparing FocusTikZ with frontier models from the GPT and Claude families. We added these comparisons and discussed the practical advantages of local deployment in terms of inference time and cost.

Thank you again for your attention and support.

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

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