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Under review as a conference paper at ICLR 2027

DOES SELF-TRAINING ON PRIVILEGED REPAIRS CLOSE REPRESENTATION GAPS? A DIAGNOSTIC EVALUATION IN FOUR DOMAINS

Abstract

Vision-language models often answer a question correctly from one representation of an object and incorrectly from an informationally equivalent one. We evaluate a strategy that turns such disagreements into supervision: the model, shown both representations and both of its traces, rewrites its failed trace, and a LoRA student that sees only the weak representation is trained to match the frozen model’s token distribution over the rewrite, alongside replay of questions it already answers correctly. The privileged context thus decides what the student is trained toward. Using Qwen3-VL-8B-Instruct across four domains (synthetic social graphs, Lichess positions, WikiTableQuestions and MolLangBench), we measure what the strategy changes relative to the frozen model and where those changes come from. It narrows the representation gap sharply on chess and graphs, where the weak representation is the image (the chess image arm gains 17 points), gives small gains on tables, and widens the gap on molecules, where the weakest representation barely moves; the representations the model already reads well change little. The gains lean toward questions that point to a specific part of the image, such as one node’s arrows or one row of the board, over questions that require searching or comparing across the whole picture, with exceptions in both directions. Against answer-only fine-tuning on the same data the results are mixed; it sometimes transfers better. Rerun from its own trained model, it improves once more and then stops. The strategy cannot supervise a representation its teacher cannot reason in, needs two additions to train stably, and can leave correct answers resting on reasoning that contradicts the data.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
Cross-modal reasoning transfer, Privileged self-distillation, Learning using privileged information, Knowledge Distillation

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_W82wOpenReview ↗
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Paper summary

The paper studies representation gaps in vision-language models: a model often answers correctly from one equivalent representation of the same input but fails from another (e.g., a social-graph image vs. its edge list). Rather than proposing a new mechanism, it diagnoses a common training recipe — privileged-repair self-training, where a frozen teacher sees both a strong and a weak representation plus its two traces, rewrites the failed trace into a correct one, and a LoRA student trained only on the weak view matches the teacher's token distribution on that rewrite while replaying questions it already answers correctly. The paper makes three contributions. First, it introduces a method-agnostic diagnostic that decomposes training gains into reading of named regions, completion rather than truncation, and shifted answer priors. Second, it releases an open four-representation dataset across four domains (social graphs, chess, tables, molecules). Third, it reports a four-domain evaluation. Validation shows the recipe narrows gaps where the weak view is an image (chess image arm rises from 41.5 to 58.5 points) but helps little on tables and even widens the gap on molecules (SMILES barely moves). Gains transfer poorly, compare mixedly against answer-only SFT, and saturate after a second round. The contribution is diagnostic and cumulative, not mechanistic.

Critical strengths

The paper turns the vague question "does privileged self-training really close representation gaps" into a quantifiable protocol: a behavioral definition of the gap (K informationally equivalent representations, question-for-question), a three-way decomposition of training gains, and a released four-representation dataset across four domains. This is a contribution the community can adopt and cite independently of this paper's specific recipe.

Critical weaknesses
  1. The statistical foundation is too thin for a diagnostic paper, which is the work's central claim. Every domain uses a single model and a single seed, with no variance, error bars, or significance testing (stated directly in §12); the anchor-loss evidence is admitted to be anecdotal (§6c), and several key deltas rest on single observations.

  2. The method-agnostic claim and the baseline reference are not actually demonstrated. The protocol is presented as a reusable, method-independent diagnostic, yet it is exercised on only one instance — privileged-repair self-training — and is never run on the closest self-/context-distillation approaches that are discussed at length in related work. Meanwhile the only benchmarked alternative is answer-only SFT, explicitly the simplest, not the strongest, baseline.

Questions for authors
  1. Can you report multi-seed results (≥3 seeds) with mean ± variance for each domain, and run a significance test on the key deltas in Table 2 and Table 4 — most importantly the chess image arm (+17.00) and the SMILES arm (+0.71)? If the sub-1-point text-arm differences (e.g., edge list −0.11, prose +0.78) do not survive across seeds, which of the paper's conclusions would you retract?
  2. The anchor-loss evidence is described as anecdotal. Can you turn it into a quantifiable controlled comparison — for example, a matched run with anchor rows removed — so that the "anchors prevent forgetting" claim is supported by measurement rather than observation?
  3. To substantiate the method-agnostic claim, could you demonstrate the diagnostic protocol on a second instance, such as context distillation or on-policy self-distillation, rather than only on privileged-repair self-training?
  4. Can you benchmark at least one of the closest self-/context-distillation methods on the same platform (same model, same pair-mining, same scoring) alongside answer-only SFT, to position this variant within the method family rather than only against the simplest baseline?
4 comments
AuthorsOpenReview ↗

More details responses to concerns raised

We thank the reviewer. Some experiments are in progress, but we are presenting some of the results we have analysed, so that the reviewer has a chance to read this. We will update this response with full response over the next few days, once we have all the results

In brief: the graph image gain, the global gain and the narrowing of the gap hold across three seeds;

W1/Q1. Multi-seed results and significance

TL;DR: Across three seeds, the graph image arm gains +7.56 ± 0.33 points (each seed p < 10⁻⁶), and global accuracy gains +1.60 ± 0.25 (each seed p ≤ 0.01). No text-arm change is significant in any seed. There are some contextual claims we have like "no strong representation falls by more than 1.22 points", we will retract those, but the overall trend of the results hold up.

Each seed changes the LoRA initialisation and the order of the training batches; Training targets are not regenerated, so the spread is training variance. All seeds are scored against the same frozen-base output graph test items.

Graph armBaseSeeds 42 / 43 / 44Mean Δ [95% CI]Per-seed McNemar pt-test p
Image63.3371.22 / 70.89 / 70.56+7.56 [+5.15, +9.89]≤ 5×10⁻⁷0.0006
Adj. list81.4480.22 / 79.67 / 80.89−1.19 [−2.81, +0.41]0.07–0.640.08
Edge list86.3386.22 / 86.00 / 85.44−0.44 [−1.74, +0.85]0.30–1.000.20
Prose86.8987.67 / 86.78 / 87.67+0.48 [−0.78, +1.70]0.34–1.000.25
Global79.5081.33 / 80.83 / 81.14+1.60 [+0.84, +2.35]≤ 0.0100.008

Similarly, for chess, the multi seed run is as follows

Chess armBaseSeeds 42 / 43 / 44Mean Δ [95% CI]Per-seed McNemar pt-test p
Image41.5058.50 / 56.40 / 58.40+16.27 [+13.77, +18.77]≤ 2×10⁻²⁰0.002
FEN55.0058.10 / 59.50 / 59.90+4.17 [+1.40, +7.13]0.005–0.070.017
Prose90.8092.70 / 92.50 / 93.00+1.93 [+0.67, +3.23]0.009–0.0530.006
Piece list95.0095.80 / 95.90 / 95.50+0.73 [−0.40, +1.90]0.20–0.550.026
Global70.5876.28 / 76.08 / 76.70+5.78 [+4.67, +6.89]≤ 1×10⁻¹⁸0.001

What we retract or revise:

  • "No strong representation falls by more than 1.22 points" (abstract, §5(c)) was a single-seed number; seed 43 drops the adjacency list by 1.78. We will say that no fall is significant, and we will report the adjacency list's decline, which is consistent across seeds, as a possible small cost.
  • All sub-1-point graph text-arm deltas will be marked as within seed variation. Ex: Graph prose +0.78 is not a gain.

W2/Q3–Q4. Method-agnostic claim and stronger baselines

TL;DR: The diagnostics now cover three methods on the same platform, not one.

  • A STaR-style control (C2, graphs; full details in our response to Reviewer 1). It uses the same model, pair mining, data budget, KL objective and scoring, but the teacher's context holds only the gold answer, with no strong representation. We have listed a clear analysis shown here that shows that though StaR gets reasonable performance boost, slightly less than ours, its reasoning trace are factually wrong in a significantly proportionate way, which makes this method more desirable. More details can be found at response to the other reviewer https://openreview.net/forum?id=GJd4AVPEKT&noteId=j1WVAgYv9I (section - W1/Q1. Is the gain due to the privileged repair?)

  • Answer-only SFT (§8) is the simplest baseline and it does quite well, atleast as per accuracy (already tabulated in the paper) : in domain it leads ours on accuracy but a lot is attributed to truncation. The truncation diagnostic at https://openreview.net/forum?id=GJd4AVPEKT&noteId=j1WVAgYv9I (Section - W3/Q2. Truncation) already explains part of that lead, since SFT always answers. Ultimately, the core motivation of the method is to have reasoning traces from different representation guide the model towards stronger understanding of the representation in self repair way, so that we will get answer along with reasoning. So, we will concede in the paper that, if accuracy and the final answer, without reasoning, is all that really matter, the better choice is SFT, not our self repair framework

AuthorsOpenReview ↗

No anchor ablation

Q2. Controlled no-anchor ablation

TL;DR: We reran the Table 2 graph run with every anchor row removed and nothing else changed. Without anchors, accuracy improves (+1.33 global), but the model forgets: Across representations, the model consistently regresses performance on questions that model got right (shown in the table) Anchors therefore do what §6(b) claimed: they prevent forgetting without limiting the repair.

Setup. The two runs differ only in their training data: one includes the anchor rows, the other trains on the teacher-repaired rows alone. Model, LoRA configuration, loss, teacher contexts, optimiser, seed, batch size and epochs are unchanged, and each repaired row is seen exactly twice in both runs.

1. Accuracy improves without anchors

Graph test accuracy (%)No anchorsWith anchors
Image72.3371.22
Adjacency list85.5680.22
Edge list86.4486.22
Prose86.3387.67
Global82.6781.33

2. But the model forgets what it already knew

Of the items the base model answered correctly, the number each run now answers wrongly:

Base-correct itemsNo anchorsWith anchors
Image (n=570)4339
Adjacency list (n=733)5117
Edge list (n=777)5616
Prose (n=782)729
All text (n=2,292)17942

What we will change in the paper. We will replace the anecdotal §6(b) with this measurement:

(b) Anchors prevent off-target forgetting. In a matched ablation that removes the anchor rows and changes nothing else (Appendix X), headline accuracy rises by 1.33 points, but the model forgets as shown in the table, that shows the model regression on answers the base model already got right. Headline accuracy alone would therefore misreport what anchors do.

Appendix X will give the full tables and the setup.

Thanks for the additional experiments. I maintain my original score.

Thank you for reading the new results. If there are specific concerns that remain that you would like addressed further, we’d be grateful to know which ones so we can address them in the revision.We thank you for the constructive feedback that helped us improve our analysis.

Reviewer_SEdQOpenReview ↗
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Paper summary

This paper studies whether a model can learn from a representation it reads well to improve on another representation of the same information. A frozen Qwen3-VL-8B-Instruct teacher sees both representations and traces, repairs the failed trace, and shortens it. A LoRA student learns from these repairs using only the weak view, alongside replay of correct examples. Gains are largest on graph and chess images. SMILES barely improves, transfer is limited, and answer-only SFT is often stronger in domain.

Critical strengths

The paper compares the same questions across four representations and four domains. It clearly reports negative results and examines truncation, answer biases, incorrect reasoning traces, and repeated training rounds. The dataset and these analyses could support useful follow-up work.

Critical weaknesses
  1. The role of privileged repair is not isolated. Table 4’s answer-only baseline changes target content, length, and loss together. Missing controls include cross-entropy training on the same short repairs, repair using only the weak view and gold answer, and direct strong-to-weak distillation without the failed trace. Answer-only SFT wins in three domains, and some gains come from fewer unfinished responses or changed answer biases. The current tests therefore do not show what comparing representations or repairing failed traces adds.

  2. The main results need stronger validation. Section 12 acknowledges test-based checkpoint selection, one seed per domain, and a graph run that changes augmentation and image budget together. Appendix D also reports 37% pair-level churn when teacher outputs are resampled. These issues matter for small gains and the stability choices based on single-seed graph runs. Although Table 6 provides item-level confidence intervals, the study needs validation-based model selection, an untouched test set, and repeated target-generation and training seeds.

  3. Better visual reading remains an interpretation. Table 5 does not control for training exposure, usable targets, answer distributions, or truncation across categories. On GVLQA-AUGLY, the gain is 2.68 points micro but only 0.49 points macro. Connectivity accounts for 56% of the data and almost the whole image gain. The authors also report changes in the tendency to answer “Yes.” Please report category-level exposure and fixed/broken answers, and add label-balanced and image-counterfactual tests to separate better reading from changed answer behavior.

Questions for authors

Please see the Weakness part.

2 comments
AuthorsOpenReview ↗

Responses to the concerns raised

We thank the reviewer for the constructive feedback. Below we address each weakness, with the key numbers given here and some fuller details linked from the other threads.

W1. Role of privileged repair

1. Cross-entropy training on the same repairs. Our objective is already a cross-entropy objective on the same repaired targets. At each token position t of the repaired target ỹ, Eq. 1 is the forward KL divergence from the frozen reference to the student, which decomposes as follows (sums over the reference's top-100 tokens V_t):

KL(P_ref ‖ P_stu) = Σ_v P_ref(v) · log [ P_ref(v) / P_stu(v) ]
                  = Σ_v P_ref(v) · log P_ref(v)  −  Σ_v P_ref(v) · log P_stu(v)
                  = −H(P_ref)  +  CE(P_ref, P_stu)

The first term is the negative entropy of the reference; the second is the cross-entropy from the reference to the student.

The reference distribution is constant throughout training. P_ref is computed by the frozen model, so H(P_ref) is therefore a constant, and

∇θ KL(P_ref ‖ P_stu) = ∇θ CE(P_ref, P_stu)

Minimising KL divergence is the same as minimizing CE.

2. Repair using only the weak view and the gold answer. This is our STaR-style control C2: the teacher sees the weak representation, its failed trace and the gold answer, but not the strong representation; everything else is unchanged. On graph images, C2 reaches 70.22% accuracy against 71.22% for ours (base 63.33%), so most of the accuracy gain does not need the strong representation, and the revision will say so. What the strong representation changes is how answers are reached: C2's count and list answers contradict its own edge claims 21.4% of the time, against 6.8% for ours. Full details: https://openreview.net/forum?id=GJd4AVPEKT&noteId=j1WVAgYv9I

3. Answer-only SFT (§8) is the simplest baseline and it does quite well, atleast as per accuracy (already tabulated in the paper) : in domain it leads ours on accuracy but a lot is attributed to truncation. The truncation diagnostic at https://openreview.net/forum?id=GJd4AVPEKT&noteId=j1WVAgYv9I (Section - W3/Q2. Truncation) already explains more. Ultimately, the core motivation of the method is to have reasoning traces from different representation guide the model towards stronger understanding of the representation in self repair way, so that we will get answer along with reasoning. So, we will concede in the paper that, if accuracy and the final answer, without reasoning, is all that really matter, the better choice is SFT, not our self repair framework

W2. Model selection based on test

For the submission, we trained the graph domain with two seeds and reported the one with the higher test accuracy; within each run, the checkpoint step was chosen on validation. We have since trained three seeds each for graphs and chess, with every checkpoint selected on validation alone. The three-seed means reproduce the reported image gains to within 0.73 points. Full details are in W4 (Part 2): https://openreview.net/forum?id=GJd4AVPEKT&noteId=zmV2Aw2Ylu

W3. Better visual reading remains an interpretation

We agree that behavioural results alone cannot establish better internal reading, but a few measurements point in that direction.

1. image counterfactual tests

  • Graphs : flip one arrow (A→B becomes B→A) or delete one, drawn on the original layout so nothing else moves.
  • Chess : remove, add or recolour a piece, or move one to an empty square; every board stays a legal position. Only the edited squares' pixels change.

The motivation of the experiment is - for the same prompt, same question, same image - with very little changes, sometimes as much as a few pixels, is the model changing its answer appropriately? If the model shows positive signs here, the model is responding to the right visual cues.

Image accuracy (%)Base, original picturesBase, edited picturesTrained, edited pictures
Graphs64.1146.4653.62
Chess40.2034.5346.96

The trained model ends up being responsive to image changes, than the base models

2. Claims about unseen test images become more accurate. Graded against the ground-truth board or edge list: on chess, true factual claims increase after our training, which is soft indication that model is improving visual reasoning. Details: https://openreview.net/forum?id=GJd4AVPEKT&noteId=j1WVAgYv9I

3. The chess gain holds on a board orientation never seen in training. SEAM draws Black-to-move boards upside down, while every board in our training had White at the bottom. The image gain is +8.7 points on these flipped boards and +7.4 on upright ones. Details in W4 (Part 1): https://openreview.net/forum?id=GJd4AVPEKT&noteId=zmV2Aw2Ylu

Separating better reading from better priors ultimately needs causal analysis, such as probing or activation patching, which we will name as an open question in §10. Further experiments on this point are in progress.

W3: Category-level exposure, fixed/broken answers, truncation and answer distributions

Following up on W3, Parts 1–3 answer each request in turn: category-level exposure and fixed/broken answers (Part 1), the label-balanced test (Part 2), and image-counterfactual tests on graphs and chess (Part 3).

TL;DR: Categories with similar shares of the training set gain very different amounts, and some small categories gain a lot, so exposure alone does not explain the category-level gains. Graphs

CategoryShare of training setΔ (accuracy boost)Fixed / broken
followees list3.6%+15.617 / 3
followers list3.5%+11.117 / 7
followees count3.4%+14.415 / 2
followers count3.0%+24.424 / 2
common follower2.2%+1.112 / 11
most followed1.7%+3.39 / 6
least followed1.7%+3.311 / 8
mutual following1.0%+4.44 / 0
edge exists0.6%+6.76 / 0
triangle ‡0.1%−5.67 / 12
total20.7%+7.9122 / 51

Chess

CategoryShare of training setΔ (accuracy boost)Fixed / broken
rank occupants3.6%+4850 / 2
file count3.0%+1519 / 4
rank count2.5%+2633 / 7
pawn count2.4%+517 / 12
piece square2.0%+2528 / 3
same colour pair1.2%+1717 / 0
most occupied file1.1%+48 / 4
square colour0.9%+1416 / 2
has piece type0.8%+712 / 5
total comparison0.6%+916 / 7
total18.2%+17.0216 / 46

1. Exposure does not explain the gains category by category. Overall, categories with more training rows tend to gain more. This is partly by construction: training rows come from the base model's failures, so categories with more room to improve get more of them. But categories with almost the same share gain very different amounts: pawn count (2.4%) gains +5 while rank count (2.5%) gains +26; common follower (2.2%) gains +1.1 while followers count (3.0%) gains +24.4. Some small categories gain a lot: same colour pair (1.2%) +17, square colour (0.9%) +14.

2. Fixed/broken answers. In most categories the checkpoint fixes far more items than it breaks (e.g., rank occupants 50 / 2, followers count 24 / 2). In a few it fixes and breaks items at similar rates: common follower 12 / 11, pawn count 17 / 12, least followed 11 / 8. There are some very rare categories, like Triangle, where it does break more than it fixes, that is driven by poor reasoning traces of the model.

W3: GVLQA-AUGLY: exposure and the label-balanced test

TL;DR: We agree the GVLQA transfer is narrow: connectivity carries almost all of the gain, and the macro gain is only +0.49. But one key thing to highlight here GVLQA is a dataset only used for test-time evaluation, its never seen during training. Connectivity is a task the model never trained on, its test set is label-balanced by construction, the gain holds on all five unseen layouts, and it holds on both "Yes" and "No" items.

Label balance. GVLQA's connectivity test set has 4,924 questions: 2,465 "Yes" and 2,459 "No" (roughly equal split). Always answering "Yes", or always "No", scores 50%.

LayoutBaseCkptΔ
circo59.4863.85+4.37
fdp60.4665.70+5.24
neato62.4168.18+5.77
sfdp60.1765.92+5.75
twopi59.9564.81+4.85
pooled60.5065.69+5.19

The table shows the gains on GVLQA are not just model learning to be biased to say 'yes' or 'no' but a more systematic learning about the problem

Reviewer_RMJsOpenReview ↗
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Paper summary

The paper asks whether a VLM can close its own representation gap, which is the accuracy spread between the best and worst of four equivalent formats of the same object, one image and three text. When Qwen3-VL-8B answers an item correctly from one format and wrongly from another, the paper calls the first the strong representation and the second the weak representation. The same frozen model is then shown both formats and both of its reasoning traces, and is asked to rewrite the failed trace so that it reaches the right answer while citing only the weak format. The paper calls this rewrite a privileged repair. After a second pass shortens it, a LoRA student that sees only the weak representation is trained to match the frozen model's token probabilities on the shortened trace, with most of each batch spent replaying items the model already answers correctly. The paper presents itself as an evaluation study rather than a new method, and it releases a dataset that gives every item in four formats, covering graphs, chess, tables and molecules.

The gains depend strongly on the domain. On chess and graphs, where the image is the weakest format, they are large, with image accuracy up 17.00 points on chess and 7.89 on graphs. Tables barely move, and the gap on molecules gets wider. Answer-only SFT does better in-domain everywhere except tables. Transfer to outside benchmarks is small, and the only clear case is GVLQA with image input, up 2.94 points and still up 2.68 on layouts not seen in training. The authors trace much of the gain to questions that name where the answer lies, to outputs that are no longer cut off and, on GVLQA, to a shift in how often the model answers yes.

Critical strengths
  • The evaluation is done carefully. Splits are made by object, every checkpoint is compared with a matched frozen base model, and overlap with MMTab, ChessQA and the held-out molecule tasks is measured rather than assumed. For example, 4,065 of the 4,333 WikiTableQuestions items in MMTab turned out to be in the paper's own splits, so that whole subset was dropped.

  • The analysis separates real gains from side effects, and negative results are reported openly. After normalizing answers and mapping multiple-choice letters back to the option text, the MMTab gain drops from 0.85 to 0.39 points. On the image inputs of the held-out MolLangBench tasks, 91 of the 102 items the trained model fixes had been cut off by the base model before it gave an answer. Other work on representation gaps could use the same checks.

  • The dataset is built with care and includes training splits. For molecules the four formats are linked through RDKit atom indices, and on the three tasks that can be recomputed, all 6,000 rows match the official answers.

Critical weaknesses
  • It is not yet clear whether the gain comes from the privileged repair itself. The only trained baseline is answer-only SFT, which changes both the training target and the loss. A run of the same pipeline without the strong representation, for example rejection sampling or STaR using only the weak representation, would help here. The paper notes that part of the gain is outputs that now finish instead of being cut off, and training on any short, correct trace of the model's own might give that without the strong representation, so I think this control is needed before the gain can be credited to the repair.

  • The faithfulness risk is discussed but not measured. The teacher is told never to hint at the other representation, so a rewritten trace can state something taken from the strong representation as if it were read from the weak one. The paper points this out in Sections 2 and 10, and its chess example, where the fix just changes f4 to d4, shows how it can happen. Apart from a prompt instruction to cite only what the weak representation shows, the only safeguard is a keyword filter for leaked phrases, which would not catch a borrowed fact. Since all four domains have structured ground truth, it should be fairly cheap to count how often the training targets contain such statements and whether the trained model learns to make them.

  • The main in-domain gains are not yet broken down with the paper's own truncation analysis. The contributions promise to report how much of the gain comes from outputs that are no longer cut off, and the text says truncation drops on chess, tables and molecules, but truncation rates before and after training are not given for each format in the four training domains. This breakdown is only done for two transfer benchmarks, ChessQA and the held-out molecule tasks. So for a result like the 17-point gain on chess images, it is hard to tell how much comes from reading the image better and how much from finishing the answer.

  • Two closely related benchmarks are missing from the related work, and the scope is somewhat narrow. IsoBench and SEAM already compare image and text versions of the same content, including graphs and chess. As far as I know neither has training splits, which would set this dataset apart, so it would be good to discuss them. All results also come from one model, so it is unclear how far the conclusions carry over to this kind of method in general, and the authors note that checkpoints were partly picked on test data, which may make the gains look somewhat larger.

Questions for authors
  • How does the method compare with rejection-sampling fine-tuning or STaR on the weak representation alone, with the same amount of data?

  • What are the truncation rates before and after training for each format in Table 2, and how do the accuracies change if you only count items that neither model cuts off?

  • Could you measure how often the rewritten targets state facts that the base model only got right from the strong representation, and whether the trained model's reasoning becomes less faithful?

2 comments
AuthorsOpenReview ↗

Further evidence to clarify some of the useful and important raised

We thank the reviewer. We ran all three requested experiments, and each will go into the revision.

W1/Q1. Is the gain due to the privileged repair? (STaR control)

TL;DR: For accuracy, mostly not. For how answers are reached, yes.

We ran C2 on graphs: STaR-style rationalisation inside our pipeline. The teacher sees the weak representation, the failed trace and the gold answer, but not the strong representation. Everything else is the same as our run: number of training examples, training mode, filters, loss and hyperparameters. The only difference C2 even just gets 238 more image targets.

Graph test, imageBaseOursC2
Accuracy63.3371.2270.22
Edge claims true of the image80.9%82.4%80.8%
Count/list answers contradicting own edge claims0.0%6.8%21.4%
Gain from answers consistent with own reasoning–+5.56+1.78

C2 − Most of the graph accuracy gain therefore does not need the strong representation, and we will say so. Without it, though, the teacher keeps the misread facts and changes only the final answer: On the train set, 54.6% of C2's count/list image targets contradict their own reasoning, against 21.5% of ours. C2 answers more often correctly without reasoning about the image better (edge claims −0.15 vs base), while ours reasons about it better (+1.48 [+0.08, +2.91]). Our contradiction rate also rises over base, but to a third of C2's. We will add C2 to Section 8 and revise the claims;

W3/Q2. Truncation

TL;DR: Image-arm gains are not a truncation effect. Two text-arm gains are.

Accuracy change overall and on items neither model truncates (same caps for both models):

ArmTrunc. base→trained (%)accuracy improvement (all)accuracy improvement (truncation excluded)
Graphs image7.0→7.3+7.89+9.14
Chess image8.6→1.8+17.00+16.26
Molecules image27.9→20.9+6.76+6.25
Chess FEN29.9→22.0+3.10−1.85
Tables CSV9.5→5.5+2.51+1.08

On every other arm the two accuracy gains by at most 1.22 points, except SMILES (+0.71 → +3.80). The full table for all 16 arms will go in Appendix C, referenced from Section 9(b).

W2/Q3. Borrowed facts and faithfulness

TL;DR: Image targets often contain borrowed facts, yet the trained model's test-time claims become more accurate. Whether its internal reading of the image improves needs mechanistic analysis.

A fact is borrowed when the failed weak-representation trace stated it wrongly and the target states it correctly. Because the representations are equivalent, the fact is true of the every representation (including image); what is borrowed is the reading. We do a short fact evalution on FEN; Graded against the FEN or edge list, 35.0% of chess and 24.3% of graph image targets contain one borrowed fact (26.6% / 20.6% over all representation). Text-arm targets rarely do (≤10.5%). The extractors grade 98.6–99.6% of strong-trace claims correct, and a manual check confirmed 39 of 42 borrowed graph facts.

If borrowing had taught the model to assert what it cannot see, its claims about unseen test images would get worse. They do improve on test images too

  • Chess: true square claims +7.77 ; pieces placed on empty squares −5.01.
  • Graphs: true edge claims +1.48; invented arrows −2.23 ; correct full follower/followee sets +5.25
  • Text arms: no significant change.

These are behavioral measurements. They cannot show whether the model's fine tuning helps reads the image better internally rather than relying on better priors, or that the model just learns shortcuts to spot these facts. That needs causal, mechanistic analysis such as probing or activation patching. We will name it as an open question in Section 10 and replace that section's qualitative discussion with these numbers.

W4. Related work and scope In progress. We will update

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W4: Related work and scope

W4 (Part 1). IsoBench, SEAM and scope

TL;DR: We will add both benchmarks to the related work. Scoring our trained checkpoints on SEAM, we find that each improves image accuracy in its own domain, and on chess the gain holds on boards drawn upside down, an orientation never seen in training. Three training seeds on graphs and chess reproduce the Table 2 image gains to within 0.73 points (Part 2).

Related work. Thank you for both pointers. We will add IsoBench (Fu et al., COLM 2024) and SEAM (Tang et al., COLM 2025) to the "Representation sensitivity" paragraph of Section 2. As you note, both are evaluation-only. Our work differs in two ways: our four domains come with training splits, and we use them to test a training strategy that targets the gap. Using the gap as a learning signal is one of the central motivations of the work.

Scope: SEAM as a further transfer test. We scored the three Table 2 checkpoints that have a SEAM counterpart, each on SEAM's matching domain (800 questions each). We used SEAM's own prompts, images, answers and scoring, under which unanswered questions count as wrong. There was no further training.

Accuracy, base → ckptTextImageText + image
Graphs70.2 → 67.427.4 → 30.865.2 → 60.6
Chess1.4 → 5.49.9 → 17.96.0 → 16.5
Chemistry13.9 → 14.025.9 → 33.024.9 → 27.5

Every checkpoint improves the image arm of its own domain, including chess positions that SEAM draws upside down (discussed below). The graph checkpoint pays for its image gain: it loses on text (−2.9) and on text plus image (−4.6). We will add these results to Section 7.

Chess: the gain holds on upside-down boards. SEAM draws every board from the side to move. In the 368 Black-to-move positions (46% of chess questions) the board is upside down: Black at the bottom, rank 1 at the top, files running h to a (checked on the images). Every board in our chess training had White at the bottom, so these positions test whether the gain survives a rendering the checkpoint never saw.

Chess, image onlynBaseCkptΔFixed / broken
White to move (orientation seen in training)43213.020.4+7.461 / 29
Black to move (board upside down)3686.214.9+8.748 / 16

The gain does not shrink on the unseen orientation: +8.7 points on flipped boards against +7.4 on upright ones.

W4 (Part 2). One model, and selection on test. On the single model, we agree, and we will scope the abstract, contributions and conclusion to Qwen3-VL-8B.Section 12’s remark that checkpoints were “partly selected on test” refers to one specific step, which we describe here. For the submission, we trained the graph domain with two seeds, which differed by about 0.5 points of variance in average accuracy. Within each run, the checkpoint step was chosen on validation accuracy. Between the two graph seeds, however, we reported the one with the higher test accuracy. That was selection on test. We couldn't do this for every domain due to the costs involved, during our submission, but our paper should have clarified this in clearer way. At the request of the reviewer W82w and to address some of the concern that your feedbacks centered on, We ended up doing 3 seeds for graphs and chess - Tables and Chemistry are still single seeds - The revised Table 2 below adds the three-seed mean. (All checkpoints are selected based on validation accuracies with no selection on test)

DomainArmBaseCkpt (Table 2)Δ3-seed meanΔ (3-seed)
Graphs (n=3,600)image63.3371.22+7.8970.89+7.56
adj. list81.4480.22−1.2280.26−1.19
edge list86.3386.22−0.1185.89−0.44
prose86.8987.67+0.7887.37+0.48
global79.5081.33+1.8381.10+1.60
Chess (n=4,000)image41.5058.50+17.0057.77+16.27
FEN55.0058.10+3.1059.17+4.17
prose90.8092.70+1.9092.73+1.93
piece list95.0095.80+0.8095.73+0.73
global70.5876.28+5.7076.35+5.78
Tables (n=12,260)col. CSV70.0272.53+2.51––
image71.3572.37+1.01––
prose76.5479.15+2.61––
JSON78.4780.16+1.70––
global74.0976.05+1.96––
Molecules (n=13,600)SMILES13.4714.18+0.71––
image31.5338.29+6.76––
mol. table47.0950.03+2.94––
prose50.2654.44+4.18––
global35.5939.24+3.65––

The above table should alleviate the concern that the checkpoint selection unfairness towards selecting models based on tests. We are happy to do more experiments, if there are further questions.

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